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Review written in collaboration with Maha Said (Orcid) and Frederique Bordignon (Orcid)
The title of the article makes a simple striking claim about the state of the scientific literature with a numerical estimate of the proportion of “fake” articles. Yet, by contrast to this title, in the text of the article, Heathers is highly critical of his own work.
James’ peer review of Heathers’ article
James Heathers often mentions the limitations of his research thus “peer-reviewing” his own article to the extent that he admits that this work is “incomplete”, “unsystematic” and “far flung”.
“This work is too incomplete to support responsible meta-analysis, and research that could more accurately define this figure does not exist yet. ~1 in 7 papers being fake represents an existential threat to the scientific enterprise.”
“While this is highly unsystematic, it produced a substantially higher figure. Correspondents reliably estimated 1-5% of all papers contain fabricated data, and 2-10% contain falsified results.”
“These values are too disparate to meta-analyze responsibly, and support only the briefest form of numerical summary: n=12 papers return n=16 individual estimates; these have a median of 13.95%, and 9 out of 16 of these estimates are between 13.4% and 16.9%. Given this, a rough approximation is that for any given corpus of papers, 1 in 7 (i.e. 14.3%) contain errors consistent with faking in at least one identifiable element.”
“The accumulation of papers collected here is, frankly, haphazard. It does not represent a mature body of literature. The papers use different methods of analyzing figures, data, or other features of scientific publications. They do not distinguish well between papers that have small problematic elements which are fake, or fake in their entirety. They analyze both small and large corpora of papers, which are in different areas of study and in journals of different scientific quality – and this greatly changes base rates;…”
“As a consequence, it would be prudent to immediately reproduce the result presented here as a formal systematic review. It is possible further figures are available after an exhaustive search, and also that pre registered analytical assumptions would modify the estimations presented.”
Heathers has also in an interview published in Retraction Watch (Chawla 2024) acknowledged pitfalls in this article such as:
“Heathers said he decided to conduct his study as a meta-analysis because his figures are “far flung.””
“They are a little bit from everywhere; it’s wildly nonsystematic as a piece of work,” he said.”
“Heathers acknowledged those limitations but argued that he had to conduct the analysis with the data that exist. “If we waited for the resources necessary to be able to do really big systematic treatments of a problem like this within a specific area, I think we’d be waiting far too long,” he said. “This is crucially underfunded.”
Built in opposition to Fanelli 2009, but it’s illogical
Heathers states in the abstract that his article is “in opposition” to Fanelli’s 2009 PloS One article (Fanelli 2009), yet that opposition is illogical and artificially constructed since there is no contradiction between 2% of scientists self-reporting having taking part in fabrication or falsification and an eventual much higher proportion of “fake scientific outputs”. Like most of what is wrong with Heather’s article, this is in fact acknowledged by the author who notes that the 2% figure “leaves us with no estimate of how much scientific output is fake” (bias in self-reporting, possibility of prolific authors, etc).
Fanelli 2009 is not cited in the way JH says it is cited
Whilst the opposition discussed above is illogical, it could be that the 2% figure is mis-cited by others as representing an estimate of fake scientific outputs thus probably underestimating the extent of fraud. Heathers suggests that this may indeed be the case, but also contradicts himself about how (Fanelli 2009), or the 2% figure coming from that publication, is typically used.
In one sentence, he writes that “the figure is overwhelmingly the salient cited fact in its 1513 citations” and that “this generally appears as some variant of “about 2% of scientists admitted to have fabricated, falsified or modified data or results at least once” (Frank et al. 2023)
whilst and in another sentence, he writes that “the typical phraseology used to express it – e.g. “the most serious types of misconduct, fabrication and falsification (i.e., data fraud), are relatively rare” (George 2016).
Those two sentences cited by Heathers are fundamentally different, the first one accurately reports that the 2% figure relates to individuals self-reporting, whilst the second one appears to relate to the prevalence of misconducts in the literature itself. How Fanelli 2009 is cited in the literature is an empirical question that can be studied by looking at citation contexts beyond the two examples given by Heathers. Given that a central justification for Heathers’ piece appears to be the misuse of this 2% figure, we sought to test whether this was the case.
A first surprise was that whilst the sentence attributed to (George 2016) can indeed be found in that publication (in the abstract), first it is not in a sentence citing (Fanelli 2009) nor the 2% figure, and, second, it is quoted selectively omitting a part of the sentence that nuances it considerably: “The evidence on prevalence is unreliable and fraught with definitional problems and with study design issues. Nevertheless, the evidence taken as a whole seems to suggest that cases of the most serious types of misconduct, fabrication and falsification (i.e., data fraud), are relatively rare but that other types of questionable research practices are quite common.” (Fanelli 2009) is discussed extensively by (George 2016), and some of the caveats, e.g. on self-reporting, are highlighted.
To go beyond those two examples, we constructed a comprehensive corpus of citation contexts, defined as the textual environment surrounding a paper's citation, including several words or sentences before and after the citation (see Methods section below). 737 citation contexts could be analysed. Out of those, the vast majority (533, or 72%) did not cite the 2% figure. Instead, they often referred to this article as a general reference together with other articles to make a broad point, or, focused on other numbers in particular those related to questionable research practices (Bordignon, Said, and Levy 2024). The 28% (204) citation contexts that did mention the 2% figure did so accurately in the majority of cases: 83% (170) of those did mention that it was self-reporting by scientists whilst 17% (34) of those, or 5% of the total citation contexts analysed were either ambiguous or misleading in that they suggested or claimed that the 2% figure related to scientific outputs.
Although the analysis above does not include all citation contexts, it is possible to conclude unambiguously that the 2% figure is not overwhelmingly the salient cited fact in relation to Fanelli 2009, and that when it is cited it is often accurately, i.e. as representing self-reporting by scientists. Whilst an exhaustive analysis is beyond the scope of this peer review, it is not uncommon to find in this corpus citations contexts that have an alarming tone about the seriousness of the problem of FFPs, e.g. “…a meta-analysis (Fanelli 2009) suggest that the few cases that do surface represent only the tip of a large iceberg." [DOI: 10.1177/0022034510384627]
Thus, the rationale for Heathers’ study appears to be misguided. The supposed lack of attention for the very serious problem of FFPs is not due to a minimisation of the situation fueled by a misinterpretation of Fanelli 2009. Importantly, even if that was the case, an attempt to draw attention by claiming that 1 in 7 papers are fake, a claim which according to the author himself is not grounded in solid facts, is not how the scientific literature should be used.
Methods for the construction of the corpus of citation contexts
We used Semantic Scholar, an academic database encompassing over 200 million scholarly documents from diverse sources including publishers, data providers, and web crawlers. Using the specific paper identifier for Fanelli's 2009 publication (d9db67acc223c9bd9b8c1d4969dc105409c6dfef), we queried the Semantic Scholar API to retrieve available citation contexts. Citation contexts were extracted from the "contexts" field within the JSON response pages, (see technical specifications).
The query looks like this: semanticscholar.org
The broad coverage of Semantic Scholar does not imply that citation contexts are always retrieved. The Semantic Scholar API provided citation contexts for only 48% of the 1452 documents citing the paper. To get more, we identified open access papers among the remaining 52% citing papers, retrieved their PDF location and downloaded the files. We used Unpaywall API, which is a database to be queried with a DOI in order to get open access information about a document. The query looks like this.
We downloaded 266 PDF files and converted them to text format using an online bulk PDF-to-text converter. These files were then processed using TXM, a specialized textual analysis tool. We used its concordancer function to identify the term "Fanelli" as a pivot term and check the reference being the good one (the 2009 paper in PlosOne). We did manual cleaning and appended the citation contexts to the previous corpus.
Through this comprehensive methodology, we ultimately identified 824 citation contexts, representing 54% (784) of all documents citing Fanelli's 2009 paper. This corpus comprised 48% of contexts retrieved from Semantic Scholar and an additional 6% obtained through semi-manual extraction from open access documents. 87 of those contexts were excluded from the analysis for a range of reasons including: context too short to conclude, language neither English nor French (shared languages of the authors of this review), duplicate documents (e.g. preprints), etc, leaving us with 737 contexts. They were first classified manually in two categories, those mentioning the 2% figure and those which did not. Then, for the first category, they were further classified manually in two categories depending on whether the figure was appropriately assigned to self-reporting of researchers or rather misleadingly suggesting that the 2% applied to research outputs.
Contributions
Investigation: FB collected the citation contexts.<br /> Data curation and formal analysis: RL and MS<br /> Writing – review & editing: RL, MS and FB
References
Bordignon, Frederique, Maha Said, and Raphael Levy. 2024. “Citation Contexts of [How Many Scientists Fabricate and Falsify Research? A Systematic Review and Meta-Analysis of Survey Data, DOI: 10.1371/Journal.Pone.0005738].” Zenodo. https://doi.org/10.5281/zenodo.14417422.
Chawla, Dalmeet Singh. 2024. “1 in 7 Scientific Papers Is Fake, Suggests Study That Author Calls ‘Wildly Nonsystematic.’” Retraction Watch (blog). September 24, 2024. https://retractionwatch.com/2024/09/24/1-in-7-scientific-papers-is-fake-suggests-study-that-author-calls-wildly-nonsystematic/.
Fanelli, Daniele. 2009. “How Many Scientists Fabricate and Falsify Research? A Systematic Review and Meta-Analysis of Survey Data.” PLOS ONE 4 (5): e5738. https://doi.org/10.1371/journal.pone.0005738.
Frank, Fabrice, Nans Florens, Gideon Meyerowitz-Katz, Jérôme Barriere, Éric Billy, Véronique Saada, Alexander Samuel, Jacques Robert, and Lonni Besançon. 2023. “Raising Concerns on Questionable Ethics Approvals - a Case Study of 456 Trials from the Institut Hospitalo-Universitaire Méditerranée Infection.” Research Integrity and Peer Review 8 (1): 9. https://doi.org/10.1186/s41073-023-00134-4.
George, Stephen L. 2016. “Research Misconduct and Data Fraud in Clinical Trials: Prevalence and Causal Factors.” International Journal of Clinical Oncology 21 (1): 15–21. https://doi.org/10.1007/s10147-015-0887-3.
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Reply to the reviewers
We thank all the reviewers for their helpful and constructive comments and for their time.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):*
Summary: Dady et al have developed fluorescent reporters to enable live imaging of cell behaviour and morphology in human pluripotent stem cell lines (PSCs). These reporters target 3 main features, the plasma membrane, nucleus and cytoskeleton. Reporter PSCs have been generated using a piggyBac transposon-mediated stable integration strategy, using a hyperactive piggyBac transposase (HyPBase). The same constructs were also used for mosaic labelling of cells within 2D cultures using lipofectamine transfection.
The reporters used are tagged with either eGFP or mKate2 (far red) and tag the plasma membrane (pm) via the addition of a 20 amino-acid sequence from rat GAP-43 to the N-terminus of the fluorescent protein, the nucleus via Histone 2B with a laser-mediated photo-conversion option (H2B-mEos3.2), and the cytoskeleton via F-Tractin. In total, the authors produced lines with the following:
• pm-mKate2 (far red) • pm-eGFP (green) • H2B-mEos3.2 (green to red) • F-tractin-mKate2 (far red) • H2B-mEos3.2 and pm-mKate2 (green to red, plus far red)
The cell lines used to generate these were the human embryonic stem cell line H9 and human induced pluripotent cell line ChiPS4. The constructs were also used to label cells in a mosaic fashion, using lipofectamine transfection of the original cell lines once they had formed neural rosettes.
Using these cells, Dady et al then performed live imaging in vitro of human spinal cord rosettes and assessed cell behaviour. In particular they analysed mitotic cleavage planes and apical positioning of neural progenitor cells (NPCs), and assessed actin dynamics within these cells. They showed a slowing of the cell cycle length after the initial expansion phase, an increase in the rate of asymmetric division of these NPCs, and abscission of the apical membrane during these divisions. The F-tractin reporter showed enrichment at the basal nuclear membrane during these cell divisions, suggested to help prevent basal chromosome displacement during mitosis.
Major comments: The data presented are convincing and could be strengthened by the following additions and clarifications:*
- How long do the fluorescent reports take to be visible when transfected via lipofectamine? How efficiently are they expressed? And what concentrations were tested to enable the mosaic expression presented? * We followed the manufacturer’s instructions for Lipofectamine 3000 transfection, using the protocol recommended for set up for a 6 wells plate. We detected fluorescence the following morning ~16h. We did not assess earlier time points or optimise efficiency as we observed the mosaic pattern of expression we set out to achieve, with small groups of labelled cells and single cells as shown in Figure 3 and movies 2 and 3. This information and the detailed protocol provided below are now included in the Methods section “Labelling individual cells in human spinal cord rosettes by lipofection”.
Manufacturer’s instructions for Lipofectamine 3000 transfection (6 well plate):
- 1 tube containing 125 ul of Opti-MEM and 7.5 ul of Lipofectamine 3000
- 1 tube containing 250 ul of Opti-MEM with 5 ug of DNA (total mix DNAs of 2 ug/ul) and P3000 Reagent
- Add diluted DNA to diluted Lipofectamine 3000 (Ratio 1:1) and incubate for 10 to 15 min at Room Temperature.
- 20 ul of DNA-Lipid complex was added to neural rosettes growing in 8 well IBIDI dishes (20 ul/well).
- The ratio of DNA (PiggyBac plasmid) and HypBase transposase was kept at 5:1 (for a final concentration of 2ug/ul).
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Cells in IBIDI dishes were left to develop in a sterile incubator overnight and mosaic fluorescence was observed the following morning (~16h post-lipofection).
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Will these cell lines and constructs be made publicly available after publication?*
The cell lines can be made available: for those reporters made in the H9 WiCell line an MTA will first have to be signed between the requesting PI and WiCell and permission for us to share the line(s) confirmed by WiCell; similarly, for reporters in ChiPS4 line an MTA will first need to be signed between the requesting PI and Cellartis/TakaraBio Europe. We will need to make a charge to cover costs. Constructs will be deposited with Addgene.
- Were the H9 and ChiPS4 lines characterised after the reporters were added to show they still proliferate/differentiate as they did prior to the reporter integration*?
In the Results we make clear that all lines created are polyclonal, with exception of a pm-eGFP ChiPS4 line, which is a monoclonal line (lines 145-150). We do not have direct data measuring cell proliferation but collected cell passaging data for all the reporter lines. This showed that they grow to similar densities at each passage compared to the parental line (this metadata is now provided as Supplementary data 1 and is cited in the Methods, line 348).
As a proof of principle for this approach, we created one monoclonal line from a polyclonal line ChIPS4-pm-eGFP. The latter was made by selecting an individual clone and this was then expanded and characterised for expression of pluripotency markers (immunocytochemistry data Figure S4), and the ability to differentiate into 3 germ layers (qPCR Supplementary data 1). This information is already cited in the Methods (Lines 358-362).
- Can the novel actin dynamics described be quantified? How many cells imaged show these novel dynamics?* Some of this quantification data was already reported in the paper (in figure 4 legend and in the Methods); we have now updated this and provide the detailed metadata in an Excel spread sheet, Supplementary data 4 (cited in the Methods, line 489)
Minor comments: 1. Some images in the figures and supplemental movies are low in resolution, for example the DAPI in Fig 4B, making it hard to distinguish individual cells. Please increase this.
We consider the DAPI labelling in Figure 4b to be clear, however, we wonder whether the reviewer was expecting to also see this combined with the other markers. We have therefore now provided these merged additional images in a revised Figure 4.
- Please show a merge of Phalloidin and F-Tractin in Fig4, this will help the colocalization to be fully appreciated.*
This has now been provided in revised Figure 4B.
- Some additional annotation on the supplemental movies would be useful to indicate to the **reader exactly what cell to follow. *
We have added indicative arrows to the movies, and note that more detailed labelling of the series of still images from these movies are provided in the main figures (Figures 3D and 4E & F).
*Reviewer #1 (Significance (Required)):
Human neurogenesis is currently poorly understood compared to many model systems used, yet key differences have already been identified between the human and the mouse, prompting the need for further investigation of human neural development. A major reason that human neurogenesis has been difficult to study is a lack of tools to enable cell morphology and behaviours to be analysed in real time.
The reporters and reporter PSC lines generated by Dady et al will allow many of these cell characteristics to be observed using live imaging. For example, the morphology of neural progenitors during and after cell divisions, how the apical and basal processes and membranes are divided, and how the actin cytoskeleton helps to regulate these processes.
*Importantly, PSC lines can be very heterogeneous, making generating reporter lines costly and time intensive. The use of these reporters with lipofectamine transfection, for a mosaic labelling, allows the visualisation of the plasma membrane, nucleus and cytoskeleton in any human PSC/NPC line, or even in human tissue cultures, without the need to generate each specific reporter line, making it a valuable tool for many labs in the field.
We strongly agree with this final point; this is a major reason for our study.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):*
The manuscript describes the generation of novel lines of human pluripotent stem cells bearing fluorescent reporters, engineered through piggyBac transposon-mediated integration. The cells are differentiated into neuronal organoids, allowing to capture cellular behaviors associated to cell division. A replating protocol allows the observation of aging neurons by reducing the thickness of the tissue thereby facilitating live imaging. The authors also leverage the transposon technology to create mosaically-labelled organoids which allows visualizing aspects of neuronal delamination, notably cytoskeleton dynamics. They discover an undescribed pattern of F-actin enrichment at the basal nuclear membrane prior to nuclear envelope breakdown.
L104-109: "Moreover, the transposon system obviates drawbacks of directly engineering endogenous proteins...". Despite the risk of endogenous protein dysfunction, directly tagging allows the full regulation of gene expression (including the promoter, the enhancers and other regulatory regions rather than a strong constitutive promoter such as CAG). In addition, the number of copies integrated and the genomic regions are variable with PB, which does not reflect the endogenous expression. This could be rephrased by nuancing the advantages and drawbacks of each approach. The PiggyBac method is easier and faster, but it results in overexpression of a tagged protein that will be expressed since the hESC state and might not reflect the expression dynamics of the endogenous protein.* We agree and have now revised this in the Introduction L109-118.
*L124-126: "To monitor cell shape and dynamics we used a plasma membrane (pm) localized protein tagged with eGFP or mKate2 (pm-eGFP or pm-mKate2)." Could the authors provide more details and a reference on the palmitoylated rat peptide use to force membrane expression? *
This information, including the peptide sequence, is provided in the Methods (L330-331), we have now added a reference addressing its role in membrane localisation PMID: 2918027.
L132-133: " Finally, to observe actin cytoskeletal dynamics we selected F-tractin, for its minimal impact on cytoskeletal homeostasis".
A recent JCB paper (https://doi.org/10.1083/jcb.202409192) suggests that "F-tractin alters actin organization and impairs cell migration when expressed at high levels". Whether the overexpression of F-tractin in hESC using a CAG promoter reflects the physiological F-actin dynamics and/or if the high levels could lead to an alteration of cell behavior should be addressed or at least discussed. The paper we cite in this sentence (Belin et al 2014) evaluates F-tractin expression against other approaches to labelling and monitoring the actin cytoskeleton and concludes that in comparison F-tractin has minimal impact.
We do appreciate that expression above the endogenous level has the potential to alter cell behaviour and have revised the paper to more explicitly acknowledge this: in the Introduction (L109-112), and in the Discussion/conclusion (L289-293) where we now note the recent advances reported in Shatskiy et al. 2025 PMID: 39928047.
“A further potential limitation of this approach is that over-expression driven by the CAG promoter might not reflect physiological protein dynamics and/or alter cell behaviour; for example, high levels of F-Tractin can impair cell migration and induce actin bundling, interestingly, this can now be minimised by removing the N-terminal region (Shatskiy et al 2025)”.
L146-147: "...to generate polyclonal cell lines selected for expression of easily detectable (medium level) fluorescence for live imaging studies". What are the criteria used to define medium level? Number of copies integrated into the genome? Or levels by FACS during clone selection?
To clarify, all the lines presented here are polyclonal, except for one clonal line, pm-eGFP in ChiPS4. The numbers of copies integrated may vary from cell to cell in polyclonal lines. In this study, we selected cells for all lines with a FACS gate and this data is presented in Figure S1 (see line 147).
L260-263: "Efficient stable integration and moderate expression levels were achieved by optimising, i) the quantity and ratio of piggyBac plasmids and transposase and ii) subsequent FACS to exclude high expressing cells, as well as iii) transfection methods, including temporally defined lipofection in hiPSC-derived tissues." The ration 5:1 is classically used for PB Transposase delivery, however there is still high variability in the number of copies integration. Lipofection in derived tissues has been shown to be challenging. Could the authors should provide quantitative data regarding the efficiency of their approaches, notably the level of mosaicism one could expect?
We provide quantitative data for the efficiency of transfection using nucleoporation assays (FACS data presented in Supplementary figure S1), which shows more than 80-90% efficiency for eGFP in 82.82% of cells, mKate2 in 92.74% of cells, and H2B-mEos3 22.75% of cells, while 13.79% of cells co-expressed pm-Kate and H2B-mEos3.2. No comparative data regarding the efficiency of the tissue Lipofection assay was collected: our goal was to label single/small numbers of cells in order to monitor individual cell behaviours, and this “inefficient labelling” was readily achieved following the manufacturer’s instructions (please see response to Review 1 point 1), further details are now provided in the Methods.
L191-194: "We further wished to monitor sub-cellular behaviour within the developing neuroepithelium. To achieve this, we devised a strategy to target a mosaic of cells in established neural rosettes using lipofection. PiggyBac constructs and HyPBase transposase were transfected into D8/D9 human spinal cord neural progenitors using lipofectamine (Felgner, et al., 1987)(Fig. 3A)." The mosaicism is not an all or nothing in this method but also leads to variations in expression levels among the positive cells. The protocol for lipofection could be better detailed to allow easy reproduction by other teams, and its expected efficiency should be discussed. It would be interesting to explore the relationship between individual cells phenotype and expression levels. Please see response to Reviewer 1 point 1 above for more detailed lipofection protocol which generated mosaic expression, this is now also included in the Methods. We agree that investigating the relationship between individual cell phenotypes and expression levels would be interesting, but we think this is beyond the scope of this paper.
Additional comments: -Did the authors perform karyotyping of the hPSCs prior to use in the differentiation protocol?
As these are polyclonal lines, we did not undertake karyotyping. This could be done for the one monoclonal line described here (pm-eGFP ChiPS4 line): we lack funds for commercial options, but we are exploring other possibilities.
-Were pluripotency assays performed after reporter lines generation?
These were carried out for the clonal pm-eGFP ChiPS4 line (lines 145-150). The latter was made by selecting an individual clone and this was then expanded and characterised for expression of pluripotency markers by IF (Figure S4), and the ability to differentiate into 3 germ layers by qPCR (Supplementary data 2). This information is provided in the Methods (Lines 358-362).
*-Did the authors measure the cell proliferation rate in H2B-overexpressing cells and controls? Since H2B plays an important role in cytokinesis, it could interfere in cell division when H2B is overexpressed (see doi: 10.3390/cells8111391). *
We did not directly measure cell division when H2B is over-expressed. However, we assessed cell -passaging time of all the transfected cell lines. This showed that they grow to similar densities at each passage compared to the parental line (this is now provided as Supplementary data 1 and is cited in the Methods, line 348). We also found no difference between apical visiting time of progenitors in spinal cord rosettes expressing pm-eGFP or H2B-mEoS3.2, further supporting the conclusion that levels of H2B-mEoS3.2 expression achieved in this line did not interfere with cell division (metadata provided in Supplementary data 3).
The authors should provide data concerning the efficiency of expression of the distinct markers after electroporation. This is provided in Supplementary Figure S1 (FACS data) and detailed above for this reviewer.
*At Fig 1C, the schematic representation describes clone selection, however in the methods it is stated (L348-349): "Sorted cells expressing medium levels of fluorescence were expanded and frozen then representative lots of each polyclonal cell line...". There is some confusion regarding which experiments were performed using polyclonal medium-level mixed populations or monoclonal populations. *
We apologise for any confusion and have revised the Figure 1C schematic to indicate that cells can be selected to either make polyclonal lines or clonal lines.
*Reviewer #2 (Significance (Required)):
The study provides novel tools, as well as elements regarding neuroepithelium biology. It is well conducted and written, and the quality of images is excellent. It reads more as a resource paper in its current version, since the observation regarding neural cell division and delamination are interesting but not deeply explored, so this review will focus on those technical aspects rather than the novelty of the biological findings.
This study would be of interests for researchers in stem cells and organoids, developmental biology, and neurosciences.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
In the manuscript, "Engineering fluorescent reporters in human pluripotent cells and strategies for live imaging human neurogenesis" the authors Dady et al. describe the adaptation of a recent advancement in transposase technology (HyPBase) as a method to integrate live reporters in human pluripotent stem cells. They show that these florescent reporters paired with new imaging strategies can be used to confirm the existence cellular behaviour described in other species such as the interkinetic nuclear migration (IKNM) of dividing progenitors in neural tube development. Finally, they demonstrate that this live imaging system is also able to discover novel biology by identifying previously undescribed actin polymerization at the basal nuclear surface of cortical progenitors undergoing cell division. Overall, the study presents two examples in which this adapted tool will aid in live-imaging studies of cellular biology.
Major Concerns: 1. This work needs more controls to properly demonstrate claims that their engineering strategy provides an advancement to current Piggyback methods. Their HyPBase strategy needs to be compared and quantified in terms of efficiency with other methods to support their claims (increased detection and reduced phototoxicity).*
We do not make specific claims for our experiments with respect to the superiority of HyPBase strategy. Our comments on this approach referred to by the reviewer here are in the Introduction (L 94-103), are supported by the literature (e.g. more stable gene expression than native piggyBac or the Tc1/mariner transposase Sleeping Beauty (Doherty, et al., 2012, Yusa, et al., 2011) and serve to explain our selection of HyPBase for our experiments. We make a case for using HyPBase as opposed to another transposase and although it would be interesting to compare efficiencies, this comment does not specify what “other methods” might be informative.
2.Throughout the manuscript more quantification is needed of the results. How many rosettes were examined? Were all the reported cells within one rosette? Were there differences between rosettes? This should be done for both the spinal and cortical differentiations.
The reviewer appears to have missed this information – we placed detailed quantifications in the figure legends (numbers of independent experiments and rosettes) and in the Methods in a specific section on Quantification of cell behaviour (L465-486), rather than in the main text. These has since been further updated and we now also provide additional metadata in the form of Excel spreadsheets for quantifications and analyses made for both spinal cord and cortical rosettes (Supplementary data 3 and 4 respectively).
Minor Comments: 1. Line 246 needs quantification shown in figures of the statements made. Specifically, how many cells were measured to get this number?
This information was provided in the figure 4 legend and we have since added numbers to these data; we were able to monitor 169 divisions in 21 rosettes; 154/166 divisions had vertical cleavage planes (symmetric) and 12/166 had horizontal cleavage planes (asymmetric).
These detailed observations were made in two independent experiments, along with observations of basal nuclear membrane F-Tractin localisation. This is noted in figure 4 legend, Methods and detailed metadata is provided in Supplementary data 4.
2.How many cells in the cortical rosettes had the enriched actin at the basal nuclear surface?
We confidently observed basal nuclear membrane F-Tractin enrichment in 141/146 divisions, for the remaining 20 cases (166-146), we could not tell whether F-Tractin is enriched or not at the basal nuclear membrane either because of low expression levels or because the basal nuclear membrane was out of focus at NEB. In 5 cases, we did not see the basal nuclear enrichment despite sufficient F-Tractin expression levels and the nucleus being in focus. We have updated the Fig4 legend excluding the non-analysable cases and see detailed metadata is provided in Supplementary data 4.
*Reviewer #3 (Significance (Required)):
General Assessment: This manuscript makes a very minor advancement in the field of stem cell engineering and developmental biology, but one that is worthy of publication with a few edits.
Advance: While PiggyBac reporters are widely used in stem cell engineering, Dady et al. demonstrate a new workflow using HyPBase which would be beneficial to the field. However, to increase this benefit, much more description and quantification of the methods would be needed. The biological advances of this manuscript are also very minor, but interesting as most of them confirm that human neural rosettes mimic many of the observed cell behaviours seen in animal models. Along these lines is the actin dynamics observation in cortical rosettes is interesting, but a preliminary observation and in need of follow up experiments.
Audience: Regardless, this technique would be of interest to the wider field of stem cell engineering.
My Expertise: Human Stem Cell Engineering, Neural Tube Development*
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Referee #1
Evidence, reproducibility and clarity
Summary:
Dady et al have developed fluorescent reporters to enable live imaging of cell behaviour and morphology in human pluripotent stem cell lines (PSCs). These reporters target 3 main features, the plasma membrane, nucleus and cytoskeleton. Reporter PSCs have been generated using a piggyBac transposon-mediated stable integration strategy, using a hyperactive piggyBac transposase (HyPBase). The same constructs were also used for mosaic labelling of cells within 2D cultures using lipofectamine transfection.
The reporters used are tagged with either eGFP or mKate2 (far red) and tag the plasma membrane (pm) via the addition of a 20 amino-acid sequence from rat GAP-43 to the N-terminus of the fluorescent protein, the nucleus via Histone 2B with a laser-mediated photo-conversion option (H2B-mEos3.2), and the cytoskeleton via F-Tractin. In total, the authors produced lines with the following:
- pm-mKate2 (far red)
- pm-eGFP (green)
- H2B-mEos3.2 (green to red)
- F-tractin-mKate2 (far red)
- H2B-mEos3.2 and pm-mKate2 (green to red, plus far red)
The cell lines used to generate these were the human embryonic stem cell line H9 and human induced pluripotent cell line ChiPS4. The constructs were also used to label cells in a mosaic fashion, using lipofectamine transfection of the original cell lines once they had formed neural rosettes.
Using these cells, Dady et al then performed live imaging in vitro of human spinal cord rosettes and assessed cell behaviour. In particular they analysed mitotic cleavage planes and apical positioning of neural progenitor cells (NPCs), and assessed actin dynamics within these cells. They showed a slowing of the cell cycle length after the initial expansion phase, an increase in the rate of asymmetric division of these NPCs, and abscission of the apical membrane during these divisions. The F-tractin reporter showed enrichment at the basal nuclear membrane during these cell divisions, suggested to help prevent basal chromosome displacement during mitosis.
Major comments:
The data presented are convincing and could be strengthened by the following additions and clarifications: 1. How long do the fluorescent reports take to be visible when transfected via lipofectamine? How efficiently are they expressed? And what concentrations were tested to enable the mosaic expression presented? 2. Will these cell lines and constructs be made publicly available after publication? 3. Were the H9 and ChiPS4 lines characterised after the reporters were added to show they still proliferate/differentiate as they did prior to the reporter integration? 4. Can the novel actin dynamics described be quantified? How many cells imaged show these novel dynamics?
Minor comments:
- Some images in the figures and supplemental movies are low in resolution, for example the DAPI in Fig 4B, making it hard to distinguish individual cells. Please increase this.
- Please show a merge of Phallodin and F-Tractin in Fig4, this will help the colocalization to be fully appreciated.
- Some additional annotation on the supplemental movies would be useful to indicate to the reader exactly what cell to follow.
Significance
Human neurogenesis is currently poorly understood compared to many model systems used, yet key differences have already been identified between the human and the mouse, prompting the need for further investigation of human neural development. A major reason that human neurogenesis has been difficult to study is a lack of tools to enable cell morphology and behaviours to be analysed in real time.
The reporters and reporter PSC lines generated by Dady et al will allow many of these cell characteristics to be observed using live imaging. For example, the morphology of neural progenitors during and after cell divisions, how the apical and basal processes and membranes are divided, and how the actin cytoskeleton helps to regulate these processes.
Importantly, PSC lines can be very heterogeneous, making generating reporter lines costly and time intensive. The use of these reporters with lipofectamine transfection, for a mosaic labelling, allows the visualisation of the plasma membrane, nucleus and cytoskeleton in any human PSC/NPC line, or even in human tissue cultures, without the need to generate each specific reporter line, making it a valuable tool for many labs in the field.
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Zwei Ex-Soldaten rechnen ab: So schlecht steht es um Deutschland wirklich
https://www.youtube.com/watch?v=kOWDBy4fbqs
Der Kipp-Punkt kommt, wenn die Kassen leer sind‼️ Dann gehen uns unsere Fachkräfte an die Gurgel‼️
selbstjustiz und revolution, das ist das einzige was hilft, alles andere ist zeitverschwendung.
4:51 Die Polizisten haben Angst, die Bürger haben Angst und das ist ja auch das Problem. Machst du jetzt irgendwas? Die sind ja nicht blöd, die kriegen deine Daten raus über die Staatsanwaltschaft, und dann auf einmal kriegst du Hausbesuche. Dasselbe Problem haben die Richter, dasselbe haben die Anwälte. Massive Einschüchterung, zumindest wenn es um Clankriminalität geht. Keiner traut sich mehr, was, also Deutschland hat fertig. Wir sind im Kriegszustand. nur hat es bis jetzt uns nur keiner gesagt.
8:05 Das Problem ist auch mit diesen Einschüchterungen, das ist eine Form der Propaganda. Man weiß, man kann gegen die Leute nichts machen, also schüchtert man sie ein. Weil dann sozusagen, oh, eine Hausdurchsuchung links oder rechts von einen. Es wird juristisch nichts passieren, aber was passiert sozial? Was passiert mit den Job? Also, bestrafe einen und züchtige Hunderte. Das ist ein reines Abschreckungsmittel, was eigentlich in diktatorischen Gefilden normalerweise angewendet wird, aber anscheinend ist unsere Politik so weit, dass sie in die Enge getrieben ist, sich von der Realität verabschiedet haben, um jetzt sozusagen auf, ich nenn es mal "alte Methoden" zurückgreift, um dort einfach an der Macht zu bleiben.
8:42 Weil das wissen wir, sei es die NGO Geschichten, sei es die vielen Skandale, die Masse wahrscheinlich von vielen vielen Amsträgern, die müssten wahrscheinlich auch im Knast landen. Ja, nur das kann man natürlich schön verheimlichen, indem man die Medien auf seiner Seite hat, die Richter, die alle auch politisch irgendwo ihre Pässe haben, ihre Parteibücher, und auf der anderen Seite mit den Medien. Also alles so ein Schornstein-Effekt, alle nutzen sich gegenseitig, und geben sich auch gegenseitig Autorität.
11:04 Vorsorgen kann bis zu einem gewissen Grad ja wirklich jeder, ne? Ja, und es geht auch nicht immer um materielle Sachen. Körperlich, Geist, Netzwerk, Austauschen. Alleine bist du in der Krise nichts. Egal, was du für ein Background hast, egal wie gut du bewaffnet bist, egal wie viel Essen du hast, jeder ist Mal krank oder müde oder angeschlagen oder verletzt. Man braucht eine Schichtfähigkeit. Man braucht vor allem spezialisierte Leute, die verschiedene Fähigkeiten machen können, sich ergänzen können als Team. Ja, was ursprünglich eigentlich so die Volksseele war. Das ist ja durch die Atomisierung, ist auch wieder so eine so eine Technik, ist ja das ausgetrieben worden, ne? Oder Entwurzelungstechniken. Damit ist natürlich die Bevölkerung komplett sozusagen, jeder gegen jeden, und nur noch Ellenbogengesellschaft, und dass man eigentlich zusammen gehört, auch dieses links und rechts, grün gegen sonst was, oben gegen unten, das sind alles Techniken, nur um eigentlich "die da oben", sage ich mal, zu schützen, dass das Volk nicht ein irgendwo vorgeht. Und du hast gefragt, wie lange geht's noch? Es geht so lange, wie wir uns das gefallen lassen, und irgendwann, irgendwann stehen Leute auf und sagen, jetzt reicht's.
12:10 Aber dieser Kippppunkt muss noch kommen, das ist das Problem an der deutschen Seele, ja, bei den Südländern ist es eher so eine Art "Tauziehen", sagt man in der Psychologie. Also, wenn sozusagen eine Reaktion kommt, Druck von Regierung, neue Steuern, dann wird direkt reagiert. Bei den Deutschen oder den, ich nenn es mal den Norddeuropäern, das ist eher so ein "Kipppunkt", da passiert nichts, passiert nichts, irgendwann reicht's und dann schnappt das um, und dann ist natürlich gleich wieder Volleskalation. Aber dieser Punkt ist noch nicht da. Wir haben noch Trinken, es gibt noch Bier, es kommt noch Fußball im Fernsehen.
13:42 190.000 zusätzliche Arbeitslose mehr als im selben Zeitpunkt im Jahr davor, aber 6,2% Arbeitslosenquote. Aber sind wir mal ehrlich, das ist ja nicht die Wahrheit. Die Wahrheit ist ja, wie viele sind in Maßnahmen, wie viele gehen im vorzeitigen Ruhstand, wenn man ehrlich ist, kann man das ja mindestens verdoppeln. Und dann hast du natürlich von den zusätzlichen Beamten, die geschaffen werden, sei es in Berlin, sei es aber auf kommunaler Ebene, ich kriege das bei mir auf kommunale Ebene mit, wie viele Menschen dort verbeamtet werden, die in der Verwaltung sitzen. Ist für mich immer unbegreiflich, weiß du. Also Beamte brauchst du maximal Richter, Staatsanwälte, Polizisten. Brauchst du keine Lehrer als Beamter in meinen Augen. Ist völliger Nonsens.
14:23 Aber es bläht sich halt komplett auf, dieser Wasserkopf, und diejenigen, die hier tatsächlich produktiv noch sind, die werden immer weniger, die werden immer mehr zur Kasse gebeten. Was habe ich mich gestern und heute mit Unternehmen unterhalten, die einfach die Schnauze voll haben und sagen, ich mach nicht mehr, ich hau ab, ihr könnt mich alle mal, und dann stehen wir da. Dann hast du eine extrem linke Bewegung. Ich glaube, gestern waren es ernsthaft die Linken in den Umfragen bei 16%, wo ich mir denke, sag mal, seid ihr alle nicht mehr ganz dicht oder was? Du kannst ja ne linke Einstellung haben. Die linke Einstellung endet für mich da, wenn man irgendwie das, weiß du, "Deutschland verrecke", "Alerta Alerta", die ganze Nummer, die ich da von morgens bis abends von irgendwelchen wirklich dummen Menschen höre, die aber auf meine Kosten leben, die vom Sozialstaat leben. Was glauben die denn, wo das herkommt?
19:42 Die sind nicht alle blöd. Das Problem ist, vielen fehlen die Fakten, vielen fehlen sachliche neutrale Fakten. Alles was, sei es über öffentlich-rechtlichen Rundfunk ist, oder über Fernsehen, Radio, sonst was, durchläuft mindestens fünf Filter. Also fünf Filter von "hier ist die Explosion", hier ist die Primärquelle, und ehe wir das sehen, lesen oder sonst was, muss es mindestens durch fünf Filter durchgehen, teilweise auch sechs oder sieben Filter, und somit ist natürlich klar, die Leute können bloß auf der Datenlage, die die bekommen, eine eine Reaktion bzw. eine Lagefeststellung, eine Entscheidung treffen. Wenn aber die Rohdaten nur Lügen sind, und die das aber nicht wissen, dann können die einfach das nicht machen. Die denken wirklich vielleicht "aus bestem Wissen und Gewissen wähle ich jetzt das", oder mache ich jetzt das, oder "die sind böse und die sind gut". Aber woher ziehen die ihre Daten? Ja, und das sind so die Sachen. Einfach mehr hinterfragen, mehr selber nachdenken. Am Ende wird man selber drauf kommen, ne? Es ist es ist nicht so komplex, nur dadurch dass jeder arbeiten ist, keine Zeit hat. Ja, und wenn er dann abends kaputt nach 10 Stunden Arbeit, vor allem die Selbständigen, das ja dann eher Halbzeit, dann fällt man nur noch ins Bett oder auf Sofa, schaut Netflix, trinkt nen Wein und dann dann fängt der nächste Tag wieder vor los, also diese Narkotisierung durch viele Informationen und aber auch Überschwemmung mit 1000 Fake News und Desinformation, dadurch können die Leute leider, muss man sagen, gar nicht so richtig das urteilen. Das ist das Problem. Diese, beim NLP heißt das ja "unbewusste Inkompetenz". Ja, sie wissen gar nicht, dass die dumm sind bzw. wissen gar nicht, dass denen irgendwas fehlt. Dazu müssten die sozusagen erstmal die richtigen Fragen stellen, um eine "bewusste Inkompetenz". "Oh, hier habe ich eine Lücke." Ja, deswegen sage ich immer, vielfältig informieren. Es es reicht heutzutage nicht einfach nur um 19 Uhr die Glotze anzumachen.
23:59 Also ich kann bloß das wiederholen, was einige Polizeipräsidenten zu mir gesagt haben, und da ging's ja einmal hier um das Beispiel Frankfurt, was sie gesagt hatten, dass die komplette Polizei und auch Bundeswehr nicht in der Lage wäre, allein gegen die Frankfurter Gangster und die Kriminellen anzugehen. Also das Gegenüber hat viel mehr Waffen, Munition, viel mehr Manpower. Von allen Behörden, die ich jemals getroffen und gesehen habe, seit 2004, sagen alle dasselbe. Sobald es kracht, nehmen Sie ihre Dienstwaffe und gehen nach Hause. Also, es ist kaum einer da, und auch viele Dienststellen sind schon infiltriert [Graue Wölfe, Bozkurt]. Auch da sind schon viele, ich sag mal, aus den Clans aus den Gangbereichen mit drin, die gezielt reingebracht wurden.
26:42 Jeder, der sich mit dieser ganzen Situation mal intensiv befasst hat, weiß das. In Deutschland denken da kaum Menschen drüber nach. Die Naivität in diesem Land ist bemerkenswert. Ich habe in meinem letzten Video das von dem Delta Force Operator eingespielt, weil er, wie er gesagt hat, die Brutalität bei unseren Menschen, und die sind ja in diesem Land, das sind nicht alle, ja, aber es sind genügend mit eingesickert, die vom islamischen Staat kommen, und so weiter. Und wenn die dann die "Leutnante" sind, sage ich mal, auf der Straße, du hast das letztes mal gesagt, da werden viele folgen, da werden viele mitmachen.
27:23 Ich habe eine Rede von dem ehemaligen Chef der Kommando Spezialkräfte, General Günzel, gehört, der gesagt hat, der Mensch ist von Natur aus schlecht und brutal. Geht es aber um religiöse Gründe, ist die Brutalität in keinster Weise in Worte zu fassen. "Dieses Bemühen um eine humane Kriegführung, wenn dieses Wort erlaubt ist, fiel jedoch regelmäßig und ironischerweise immer dann sofort wieder in sich zusammen, wenn das Volk im Namen Gottes zu den Waffen gerufen wurde. Glaubenskriege und Kreuzzüge waren die mit Abstand grausamsten der Menschheitsgeschichte."
28:52 Die iranische Führung hat jetzt offiziell den heiligen Krieg erklärt gegen Israel und Amerika.
29:36 Wann geht's hier richtig los? Wenn sozusagen der Heilige Krieg, also zwischen Christen und Juden gegen Muslime bzw. Muslime gegen die Christen und Juden, dann wird es hier verdammt eng.
33:26 Lass uns den Menschen noch ein bisschen Hoffnung machen. Dass es knallen wird, das ist klar. Aber wahrscheinlich brauchen wir so ein "Reinigungsgewitter" wie Marc Friedrich, ich habe mit dem auch gestern noch so ein Interview gemacht, ganz interessant, der beschrieben. Es geht immer in Zyklen, alle 80 Jahre, und ich glaube er hat einfach recht. Ja und wir sind jetzt einfach dran. Die Frage ist, wie schlimm wird's? Die Frage ist, wie kommen wir da durch, und dann wie kommen wir auch schnell wieder nach oben? Weil wirtschaftlich ist ist hat Deutschland fertig. Hat Deutschland wirklich fertig. Das ist einfach wahr. Und das das kommt auch nicht zurück. Die Firmen, die weg sind, kommen kommen nicht wieder. Die Facharbeiter, die weg sind, kommen nicht wieder. Und ich glaube ja, da hat das, was Marc Friedrich wahrscheinlich gemeint hat, ist "das Prinzip der vier Generation" [good times create weak men…], was einfach wiederkehrend in der Geschichte der Menschheit immer wieder da ist. Und ja, ich glaube, wir brauchen es, und ich hoffe einfach noch, dass ein bisschen Restfunke, sage ich mal, unsere Ahnen irgendwie in uns drin ist, zwischen Dichtern, Denkern und auch Kämpfern. Ja, die German waren ist nicht unbedingt nur Leute, die da ganze Zeit Gedichte geschrieben haben. Ja, also auch das Wehrhafte, hoffe ich, dass das irgendwann mal wieder zurückkommt, und dann werden wir das sehen. Also, ich denke, wir zwei sehen uns dann irgendwann mal auf der Straße wieder, an der Seite von denjenigen, die Schutz brauchen. Ja, aber ich weiß nicht, wer sonst noch da ist. Das das ist genau der Punkt. Einige Kämpfer gibt es in diesem Land noch, und ich weiß, wenn wir uns auf der Straße treffen sollten, dass ich mich auf dich verlassen kann. Mein Lieber, grüß bitte alle deine Mitstreiter, weil es gibt noch genügend in diesem Land, die dieses Land lieben und nicht zum Kotzen finden ("Warum bist denn du heute hier? - Alerta Alerta!") und Deutschland nicht den Tod wünschen ("Deutschland verrecke") und von daher glaube ich schon, dass wir am Ende irgendwie wieder vernünftig vorgehen können, mein Lieber. Vielen Dank, Andre.
35:22 "Glaubenskriege und Kreuzzüge waren die mit Abstand grausamsten der Menschheitsgeschichte. Denn hier kämpfte man ja nicht mehr gegen einen, wenn auch feindlich gesonnenen, aber doch immerhin menschlichen Gegner. Hier kämpfte man gegen den Leibhaftigen mit seinem gesamten höllischen Anhang. Hier ging es nicht mehr um irdische Güter, um Land, Macht oder Interessen. Hier ging es um das Wort und die Werke des wahren Gottes. Nicht um Sieg oder Niederlage, sondern um die Ausrottung des Bösen schlechthin. Und da aber natürlich auch jedes Mittel recht, denn wer mit Gott im Bunde war, der konnte ja nichts Unrechtes tun."
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Author response:
The following is the authors’ response to the previous reviews
Public Reviews:
Reviewer #1 (Public review):
Summary:
In this manuscript, Azlan et al. identified a novel maternal factor called Sakura that is required for proper oogenesis in Drosophila. They showed that Sakura is specifically expressed in the female germline cells. Consistent with its expression pattern, Sakura functioned autonomously in germline cells to ensure proper oogenesis. In sakura KO flies, germline cells were lost during early oogenesis and often became tumorous before degenerating by apoptosis. In these tumorous germ cells, piRNA production was defective and many transposons were derepressed. Interestingly, Smad signaling, a critical signaling pathway for the GSC maintenance, was abolished in sakura KO germline stem cells, resulting in ectopic expression of Bam in whole germline cells in the tumorous germline. A recent study reported that Bam acts together with the deubiquitinase Otu to stabilize Cyc A. In the absence of sakura, Cyc A was upregulated in tumorous germline cells in the germarium. Furthermore, the authors showed that Sakura co-immunoprecipitated Otu in ovarian extracts. A series of in vitro assays suggested that the Otu (1-339 aa) and Sakura (1-49 aa) are sufficient for their direct interaction. Finally, the authors demonstrated that the loss of otu phenocopies the loss of sakura, supporting their idea that Sakura plays a role in germ cell maintenance and differentiation through interaction with Otu during oogenesis.
Strengths:
To my knowledge, this is the first characterization of the role of CG14545 genes. Each experiment seems to be well-designed and adequately controlled
Weaknesses:
However, the conclusions from each experiment are somewhat separate, and the functional relationships between Sakura's functions are not well established. In other words, although the loss of Sakura in the germline causes pleiotropic effects, the cause-and-effect relationships between the individual defects remain unclear.
Comments on latest version:
The authors have attempted to address my initial concerns with additional experiments and refutations. Unfortunately, my concerns, especially my specific comments 1-3, remain unaddressed. The present manuscript is descriptive and fails to describe the molecular mechanism by which Sakura exerts its function in the germline. Nevertheless, this reviewer acknowledges that the observed defects in sakura mutant ovaries and the possible physiological significance of the Sakura-Out interaction are worth sharing with the research community, as they may lay the groundwork for future research in functional analysis.
We thank the reviewer for valuable comments. We would like to investigate the molecular mechanism by which Sakura exerts its function in the germline in near future studies.
Reviewer #2 (Public review):
In this study, the authors identified CG14545 (named it sakura), as a key gene essential for Drosophila oogenesis. Genetic analyses revealed that Sakura is vital for both oogenesis progression and ultimate female fertility, playing a central role in the renewal and differentiation of germ stem cells (GSC).
The absence of Sakura disrupts the Dpp/BMP signaling pathway, resulting in abnormal bam gene expression, which impairs GSC differentiation and leads to GSC loss. Additionally, Sakura is critical for maintaining normal levels of piRNAs. Also, the authors convincingly demonstrate that Sakura physically interacts with Otu, identifying the specific domains necessary for this interaction, suggesting a cooperative role in germline regulation. Importantly, the loss of otu produces similar defects to those observed in sakura mutants, highlighting their functional collaboration.
The authors provide compelling evidence that Sakura is a critical regulator of germ cell fate, maintenance, and differentiation in Drosophila. This regulatory role is mediated through modulation of pMad and Bam expression. However, the phenotypes observed in the germarium appear to stem from reduced pMad levels, which subsequently trigger premature and ectopic expression of Bam. This aberrant Bam expression could lead to increased CycA levels and altered transcriptional regulation, impacting piRNA expression. In this revised manuscript, the authors further investigated whether Sakura affects the function of Orb, a binding partner they identified, in deubiquitinase activity when Orb interacts with Bam.
We appreciate the authors' efforts to address all our comments. While these revisions have greatly improved the clarity of certain sections, some of the concerns remain unclear, while details mentioned in the responses about these studies should be incorporated in the manuscript. Specifically, the manuscript still lacks the demonstration that Sakura co-localizes with Orb/Bam despite having the means for staining and visualization. This would bring insight into the selective binding of Orb with Bam vs. Sakura perhaps at different stages of oogenesis. Such analyses would allow for more specific conclusions, further alluding to the underlying mechanism, rather than the general observations currently presented.
This elaborate study will be embraced by both germline-focused scientists and the developmental biology community.
We thank the reviewer for valuable comments. We believe that the author meant Otu, not Orb, for the binding partner of Sakura that we identified. We would like to investigate the colocalization of Sakura with other proteins including Otu and the molecular mechanism by which Sakura exerts its function in the germline in near future studies.
Reviewer #3 (Public review):
In this very thorough study, the authors characterize the function of a novel Drosophila gene, which they name Sakura. They start with the observation that sakura expression is predicted to be highly enriched in the ovary and they generate an anti-sakura antibody, a line with a GFP-tagged sakura transgene, and a sakura null allele to investigate sakura localization and function directly. They confirm the prediction that it is primarily expressed in the ovary and, specifically, that it is expressed in germ cells, and find that about 2/3 of the mutants lack germ cells completely and the remaining have tumorous ovaries. Further investigation reveals that Sakura is required for piRNA-mediated repression of transposons in germ cells. They also find evidence that sakura is important for germ cell specification during development and germline stem cell maintenance during adulthood. However, despite the role of sakura in maintaining germline stem cells, they find that sakura mutant germ cells also fail to differentiate properly such that mutant germline stem cell clones have an increased number of "GSC-like" cells. They attribute this phenotype to a failure in the repression of Bam by dpp signaling. Lastly, they demonstrate that sakura physically interacts with otu and that sakura and otu mutants have similar germ cell phenotypes. Overall, this study helps to advance the field by providing a characterization of a novel gene that is required for oogenesis. The data are generally high-quality and the new lines and reagents they generated will be useful for the field.
Comments on latest version:
With these revisions, the authors have addressed my main concerns.
We thank the reviewer for valuable comments.
Recommendations for the authors:
Reviewer #2 (Recommendations for the authors):
The manuscript is much improved based on the changes made upon recommendations from the reviewers.
Though most of our comments have been addressed, we have a few more we wish to recommend. For previous points we made, we replied with further clarification for the authors.
Figure 1
(1) B should be the supplemental figure.
We moved the former Fig 1B to Supplemental Figure 1.
• Previous Fig1B (sakura mRNA expression level) is now Fig S2, not S1. Please make this data as Fig S1.
We moved Fig S1 to main Fig7A and renumbered Fig S2-S16 to Fig S1-S15.
(2) C - How were the different egg chamber stages selected in the WB? Naming them 'oocytes' is deceiving. Recommend labeling them as 'egg chambers', since an oocyte is claimed to be just the one-cell of that cyst.
We changed the labeling to egg chambers.
• The labels on lanes for Stages 12-13 and Stage 14, still only say "chambers", not "egg chambers". Also there is no Stage 1-3 egg chamber. More accurately, the label should be "Germarium - Stage 11 egg chambers".
We updated the lables on lanes as suggested by the reviewer.
(3) Is the antibody not detecting Sakura in IF? There is no mention of this anywhere in the manuscript.
While our Sakura antibody detects Sakura in IF, it seems to detect some other proteins as well. Since we have Sakura-EGFP fly strain (which fully rescues sakuranull phenotypes) to examine Sakura expression and localization without such non-specific signal issues, we relied on Sakura-EGFP rather than anti-Sakura antibodies for IF.
• Please put this info into the Methods section.
We added this info into the Methods section.
(4) Expand on the reliance of the sakura-EGFP fly line. Does this overexpression cause any phenotypes?
sakura-EGFP does not cause any phenotypes in the background of sakura[+/+] and sakura[+/-].
• Please add this detail into the manuscript.
We added this info into the Methods section.
Figure 5
(1) D - It might make more sense if this graph showed % instead of the numbers.
We did not understand the reviewer's point. We think using numbers, not %, makes more sense.
• Having a different 'n' number for each experiment does not allow one to compare anything except numbers of the egg chambers. This must be normalized.
We still don’t agree with the reviewer. In Fig 5D, we are showing the numbers of stage 14 oocytes per fly (= per a pair of ovaries). ‘n’ is the number of flies (= number of a pair of ovaries) examined. We now clarified this in the figure legend. Different ‘n’ number does not prevent us from comparing the numbers of stage 14 oocytes per fly. Therefore, we would like to show as it is now.
(2) Line 213 - explain why RNAi 2 was chosen when RNAi 1 looks stronger.
Fly stock of RNAi line 2 is much healthier than RNAi line 1 (without being driven Gal4) for some reasons. We had a concern that the RNAi line 1 might contain an unwanted genetic background. We chose to use the RNAi 2 line to avoid such an issue.
• Please add this information to the manuscript.
We added this info into the Methods section.
Figure 7/8 - can go to Supplemental.
We moved Fig 8 to supplemental. However, we think Fig 7 data is important and therefore we would like to present them as a main figure.
• Current Fig S1 should go to Fig 7, to better understand the relationship between pMad and Bam expression.
We moved Fig S1 to main Fig7A and renumbered Fig S2-S16 to Fig S1-S15.
Figure 9C - Why the switch to S2 cells? Not able to use the Otu antibody in the IP of ovaries?
We can use the Otu antibody in the IP of ovaries. However, in anti-Sakura Western after anti Otu IP, antibody light chain bands of the Otu antibodies overlap with the Sakura band. Therefore, we switched to S2 cells to avoid this issue by using an epitope tag.
• Please add this info to the Methods section.
We added this info into the Methods section.
Figure 10- Some images would be nice here to show that the truncations no longer colocalize.
We did not understand the reviewer's points. In our study, even for the full-length proteins. We have not shown any colocalization of Sakura and Otu in S2 cells or in ovaries, except that they both are enriched in developing oocytes in egg chambers.
• Based on your binding studies, we would expect them to colocalize in the egg chamber, and since there are antibodies and a GFP-line available, it would be important to demonstrate that via visualization.
As we wrote in the response and now in the manuscript, our antibodies are not best for immunostaining. We will try to optimize the experimental conditions in the future studies.
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Reviewer #2 (Public review):
In this manuscript, Ross and Miscik et. al described the phenotypic discrepancies between F0 zebrafish mosaic mutant ("CRISPants") and morpholino knockdown (Morphant) embryos versus a set of 5 different loss-of-function (LOF) stable mutants in one particular gene involved in hepatic stellate cells development: podxl. While transient LOF and mosaic mutants induced a decrease of hepatic stellate cells number stable LOF zebrafish did not. The authors analyzed the molecular causes of these phenotypic differences and concluded that LOF mutants are genetically compensated through the upregulation of the expression of many genes. Additionally, they ruled out other better-known and described mechanisms such as the expression of redundant genes, protein feedback loops, or transcriptional adaptation.
While the manuscript is clearly written and conclusions are, in general, properly supported, there are some aspects that need to be further clarified and studied.
(1) It would be convenient to apply a method to better quantify potential loss-of-function mutations in the CRISPants. Doing this it can be known not only percentage of mutations in those embryos but also what fraction of them are actually generating an out-of-frame mutation likely driving gene loss of function (since deletions of 3-6 nucleotides removing 1-2 aminoacid/s will likely not have an impact in protein activity, unless that this/these 1-2 aminoacid/s is/are essential for the protein activity). With this, the authors can also correlate phenotype penetrance with the level of loss-of-function when quantifying embryo phenotypes that can help to support their conclusions.
(2) It is unclear that 4.93 ng of morpholino per embryo is totally safe. The amount of morpholino causing undesired effects can differ depending on the morpholino used. I would suggest performing some sanity check experiments to demonstrate that morpholino KD is not triggering other molecular outcomes, such as upregulation of p53 or innate immune response.
(3) Although the authors made a set of controls to demonstrate the specificity of the CRISPant phenotypes, I believe that a rescue experiment could be beneficial to support their conclusions. Injecting an mRNA with podxl ORF (ideally with a tag to follow protein levels up) together with the induction of CRISPants could be a robust manner to demonstrate the specificity of the approach. A rescue experiment with morphants would also be good to have, although these are a bit more complicated, to ultimately demonstrate the specificity of the approach.
(4) In lines 314-316, the authors speculate on a correlation between decreased HSC and Podxl levels. It would be interesting to actually test this hypothesis and perform RT-qPCR upon CRISPant induction or, even better and if antibodies are available, western blot analysis.
(5) Similarly, in lines 337-338 and 342-344, the authors discuss that it could be possible that genes near to podxl locus could be upregulated in the mutants. Since they already have a transcriptomic done, this seems an easy analysis to do that can address their own hypothesis.
(6) Figures 4 and 5 would be easier to follow if panels B-F included what mutants are (beyond having them in the figure legend). Moreover, would it be more accurate and appropriate if the authors group all three WT and mutant data per panel instead of showing individual fish? Representing technical replicates does not demonstrate in vivo variability, which is actually meaningful in this context. Then, statistical analysis can be done between WT and mutant per panel and per set of primers using these three independent 3-month-old zebrafish.
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Author response:
Reviewer #1 (Public review):
Summary:
The manuscript by Ross, Miscik, and others describes an intriguing series of observations made when investigating the requirement for podxl during hepatic development in zebrafish. Podxl morphants and CRISPants display a reduced number of hepatic stellate cells (HSCs), while mutants are either phenotypically wild type or display an increased number of HSCs.
The absence of observable phenotypes in genetic mutants could indeed be attributed to genetic compensation, as the authors postulate. However, in my opinion, the evidence provided in the manuscript at this point is insufficient to draw a firm conclusion. Furthermore, the opposite phenotype observed in the two deletion mutants is not readily explainable by genetic compensation and invokes additional mechanisms.
Major concerns:
(1) Considering discrepancies in phenotypes, the phenotypes observed in podxl morphants and CRISPants need to be more thoroughly validated. To generate morphants, authors use "well characterized and validated ATG Morpholino" (lines 373-374). However, published morphants, in addition to kidney malformations, display gross developmental defects including pericardial edema, yolk sack extension abnormalities, and body curvature at 2-3 dpf (reference 7 / PMID: 24224085). Were these gross developmental defects observed in the knockdown experiments performed in this paper? If yes, is it possible that the liver phenotype observed at 5 dpf is, to some extent, secondary to these preceding abnormalities? If not, why were they not observed? Did kidney malformations reproduce? On the CRISPant side, were these gross developmental defects also observed in sgRNA#1 and sgRNA#2 CRISPants? Considering that morphants and CRISPants show very similar effects on HSC development and assuming other phenotypes are specific as well, they would be expected to occur at similar frequencies. It would be helpful if full-size images of all relevant morphant and CRISPant embryos were displayed, as is done for tyr CRISPant in Figure S2. Finally, it is very important to thoroughly quantify the efficacy of podxl sgRNA#1 and sgRNA#2 in CRISPants. The HRMA data provided in Figure S1 is not quantitative in terms of the fraction of alleles with indels. Figure S3 indicates a very broad range of efficacies, averaging out at ~62% (line 100). Assuming random distribution of indels among cells and that even in-frame indels result in complete loss of function (possible for sgRNA#1 due to targeting the signal sequence), only ~38% (.62*.62) of all cells will be mutated bi-allelically. That does not seem sufficient to reliably induce loss-of-function phenotypes. My guess is that the capillary electrophoresis method used in Figure S3 underestimates the efficiency of mutagenesis, and that much higher mutagenesis rates would be observed if mutagenesis were assessed by amplicon sequencing (ideally NGS but Sanger followed by deconvolution analysis would suffice). This would strengthen the claim that CRISPant phenotypes are specific.
The reviewer points out some excellent caveats regarding the morphant experiments. We agree that at least some of the effects of the podxl morpholino may be related to its effects on kidney development and/or gross developmental defects that impede liver development. Because of these limitations, we focused our experiments on analysis of CRISPant and mutant phenotypes, including showing that podxl (Ex1(p)_Ex7Δ) mutants are resistant to CRISPant effects on HSC number when injected with sgRNA#1. We did not observe any gross morphologic defects in podxl CRISPants. Liver size was not significantly altered in podxl CRISPants (Figure 2A). We will add brightfield images of podxl CRISPant larvae to the supplemental data for the revised manuscript.
We agree with the reviewer that HRMA is not quantitative with respect to the fraction of alleles with indels and that capillary electrophoresis likely underestimates mutagenesis efficiency. Nonetheless, even with 100% mutation efficiency, podxl CRISPant knockdown, like most CRISPR knockdowns, would not represent complete loss of function: ~1/3 of alleles will contain in-frame mutations and likely retain at least some gene function, so ~1/3*1/3 = 1/9 of cells will have no out-of-frame indels and contain two copies of at least partially functional podxl and ~2/3*2/3 = 4/9 of cells will have one out-of-frame indel and one copy of at least partially functional podxl. Thus, the decreased HSCs we observe with podxl CRISPant likely represents a partial loss-of-function phenotype in any case.
(2) In addition to confidence in morphant and CRISPant phenotypes, the authors' claim of genetic compensation rests on the observation that podxl (Ex1(p)_Ex7Δ) mutants are resistant to CRISPant effect when injected with sgRNA#1 (Figure 3L). Considering the issues raised in the paragraph above, this is insufficient. There is a very straightforward way to address both concerns, though. The described podxl(-194_Ex7Δ) and podxl(-319_ex1(p)Δ) deletions remove the binding site for the ATG morpholino. Therefore, deletion mutants should be refractive to the Morpholino (specificity assessment recommended in PMID: 29049395, see also PMID: 32958829). Furthermore, both deletion mutants should be refractive to sgRNA#1 CRISPant phenotypes, with the first being refractive to sgRNA#2 as well.
The reviewer proposes elegant experiments to address the specificity of the morpholino. For the revision, we plan to perform additional morpholino studies, including morpholino injections of podxl mutants and assessment of tp53 and other immune response/cellular stress pathway genes in podxl morphants.
Reviewer #2 (Public review):
In this manuscript, Ross and Miscik et. al described the phenotypic discrepancies between F0 zebrafish mosaic mutant ("CRISPants") and morpholino knockdown (Morphant) embryos versus a set of 5 different loss-of-function (LOF) stable mutants in one particular gene involved in hepatic stellate cells development: podxl. While transient LOF and mosaic mutants induced a decrease of hepatic stellate cells number stable LOF zebrafish did not. The authors analyzed the molecular causes of these phenotypic differences and concluded that LOF mutants are genetically compensated through the upregulation of the expression of many genes. Additionally, they ruled out other better-known and described mechanisms such as the expression of redundant genes, protein feedback loops, or transcriptional adaptation.
While the manuscript is clearly written and conclusions are, in general, properly supported, there are some aspects that need to be further clarified and studied.
(1) It would be convenient to apply a method to better quantify potential loss-of-function mutations in the CRISPants. Doing this it can be known not only percentage of mutations in those embryos but also what fraction of them are actually generating an out-of-frame mutation likely driving gene loss of function (since deletions of 3-6 nucleotides removing 1-2 aminoacid/s will likely not have an impact in protein activity, unless that this/these 1-2 aminoacid/s is/are essential for the protein activity). With this, the authors can also correlate phenotype penetrance with the level of loss-of-function when quantifying embryo phenotypes that can help to support their conclusions.
Reviewer #2 raises an excellent point that is similar to Reviewer #1’s first concern. Please see our response above. In general, we agree that correlating phenotype penetrance with level of loss-of-function is a very good way to support conclusions regarding specificity in knockdown experiments. Unfortunately, because the phenotype we are examining (HSC number) has a relatively large standard deviation even in control/wildtype larvae (for example, 63 ± 19 (mean ± standard deviation) HSCs per liver in uninjected control siblings in Figure 1) it would be technically very difficult to do this experiment for podxl.
(2) It is unclear that 4.93 ng of morpholino per embryo is totally safe. The amount of morpholino causing undesired effects can differ depending on the morpholino used. I would suggest performing some sanity check experiments to demonstrate that morpholino KD is not triggering other molecular outcomes, such as upregulation of p53 or innate immune response.
Reviewer #2 raises an excellent point that is similar to Reviewer #1’s second concern. Please see our response above. We acknowledge that some of the effects of the podxl morpholino may be non-specific. To address this concern in the revised manuscript, we plan to perform additional morpholino studies, including morpholino injections of podxl mutants and assessment of tp53 and other immune response/cellular stress pathway genes in podxl morphants.
(3) Although the authors made a set of controls to demonstrate the specificity of the CRISPant phenotypes, I believe that a rescue experiment could be beneficial to support their conclusions. Injecting an mRNA with podxl ORF (ideally with a tag to follow protein levels up) together with the induction of CRISPants could be a robust manner to demonstrate the specificity of the approach. A rescue experiment with morphants would also be good to have, although these are a bit more complicated, to ultimately demonstrate the specificity of the approach.
(4) In lines 314-316, the authors speculate on a correlation between decreased HSC and Podxl levels. It would be interesting to actually test this hypothesis and perform RT-qPCR upon CRISPant induction or, even better and if antibodies are available, western blot analysis.
We appreciate the reviewer’s acknowledgement of the controls we performed to demonstrate the specificity of the CRISPant phenotypes. The proposed experiments (rescue, assessment of Podxl levels) would help bolster our conclusions but are technically difficult due to the relatively large standard deviation for the HSC number phenotype even in wildtype larvae and the lack of well-characterized zebrafish antibodies against Podxl.
(5) Similarly, in lines 337-338 and 342-344, the authors discuss that it could be possible that genes near to podxl locus could be upregulated in the mutants. Since they already have a transcriptomic done, this seems an easy analysis to do that can address their own hypothesis.
Thank you for this suggestion. We were referring in these sections to genes that are near the podxl locus with respect to three-dimensional chromatin structure; such genes would not necessarily be near the podxl locus on chromosome 4. We will clarify the text in this paragraph for the revised manuscript. At the same time, we will examine our transcriptomic data to check expression of mkln1, cyb5r3, and other nearby genes on chromosome 4 as suggested and include this analysis in the revised manuscript.
(6) Figures 4 and 5 would be easier to follow if panels B-F included what mutants are (beyond having them in the figure legend). Moreover, would it be more accurate and appropriate if the authors group all three WT and mutant data per panel instead of showing individual fish? Representing technical replicates does not demonstrate in vivo variability, which is actually meaningful in this context. Then, statistical analysis can be done between WT and mutant per panel and per set of primers using these three independent 3-month-old zebrafish.
Thank you for this suggestion. We will modify these figures to clarify our results.
Reviewer #3 (Public review):
Summary:
Ross et al. show that knockdown of zebrafish podocalyxin-like (podxl) by CRISPR/Cas or morpholino injection decreased the number of hepatic stellate cells (HSC). The authors then generated 5 different mutant alleles representing a range of lesions, including premature stop codons, in-frame deletion of the transmembrane domain, and deletions of the promoter region encompassing the transcription start site. However, unlike their knockdown experiment, HSC numbers did not decrease in podxl mutants; in fact, for two of the mutant alleles, the number of HSCs increased compared to the control. Injection of podxl CRISPR/Cas constructs into these mutants had no effect on HSC number, suggesting that the knockdown phenotype is not due to off-target effects but instead that the mutants are somehow compensating for the loss of podxl. The authors then present multiple lines of evidence suggesting that compensation is not exclusively due to transcriptional adaptation - evidence of mRNA instability and nonsense-mediated decay was observed in some but all mutants; expression of the related gene endoglycan (endo) was unchanged in the mutants and endo knockdown had no effect on HSC numbers; and, expression profiling by RNA sequencing did not reveal changes in other genes that share sequence similarity with podxl. Instead, their RNA-seq data showed hundreds of differentially expressed genes, especially ECM-related genes, suggesting that compensation in podxl mutants is complex and multi-genic.
Strengths:
The data presented is impressively thorough, especially in its characterization of the 5 different podxl alleles and exploration of whether these mutants exhibit transcriptional adaptation.
Thank you very much for appreciating the hard work that went into this manuscript.
Weaknesses:
RNA sequencing expression profiling was done on adult livers. However, compensation of HSC numbers is apparent by 6 dpf, suggesting compensatory mechanisms would be active at larval or even embryonic stages. Although possible, it's not clear that any compensatory changes in gene expression would persist to adulthood.
This reviewer makes an excellent point. Our finding that the largest changes in gene expression were in extracellular matrix (ECM) genes and ECM modulation is a major function of HSCs supports the hypothesis that genetic compensation is occurring in adults. Nonetheless, we agree that compensatory changes in adults may not fully reflect the compensatory changes during development, so it would bolster the conclusions of the paper to perform the RNA sequencing and qPCR experiments on zebrafish larval livers.
We tried very hard to do this experiment proposed by Reviewer #3. In our hands, obtaining sufficient high-quality RNA for robust gene expression analysis typically requires pooling of ~10-15 larval livers. These larvae need to be obtained from a heterozygous in-cross in order to have matched wildtype sibling controls. Livers must be dissected from freshly euthanized (not fixed) zebrafish. Thus, this experiment requires genotyping live, individual larvae from a small amount of tissue (without sacrificing the larvae) before dissecting and pooling the livers. Unfortunately we were unable to confidently and reproducibly genotype individual live podxl larvae with these small amounts of tissue despite trying multiple approaches. Therefore we were not able to perform gene expression analysis on podxl mutant larval livers.
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- Jun 2025
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can we add a new tag called download disputes report?
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Reply to the reviewers
Revision Plan
June 28, 2025
Manuscript number: RC-2025-02982
Corresponding author(s): Babita Madan, Nathan Harmston, David Virshup
General Statements In Wnt signaling, the relative contributions of ‘canonical (β-catenin dependent) and non- canonical (β-catenin independent) signaling remains unclear. Here, we exploited a unique and highly robust in vivo system to study this. Our study is therefore the first comprehensive analysis of the β-catenin independent arm of the Wnt signaling pathway in a cancer model and illustrates how a combination of cis-regulatory elements can determine Wnt-dependent gene regulation.
We are very pleased with the reviews; it appears we communicated our goal and our findings clearly, and in general the reviewers felt the study provided important information, was well planned and the results were “crystal clear”.
While more experiments could strengthen and extend the results, we feel our results are already very robust due to the use of multiple replicates in the in vivo system.
The Virshup lab in Singapore closed July 1, 2025 and so additional wet lab studies are not feasible.
- Description of the planned revisions
Insert here a point-by-point reply that explains what revisions, additional experimentations and analyses are planned to address the points raised by the referees.
Below we address the points raised by the reviewers:
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
…
The article has the merit of addressing a yet-unsolved question in the field (if beta-catenin can also repress genes) that only a limited number of studies has tried to tackle, and provides useful datasets for the community. The system employed is elegant, and the PORCN-inhibition bypassed by a ____constitutively active beta-catenin is clean and ingenious. The manuscript is clearly written.
We thank the reviewers for their kind comments on the importance of the data. Our orthotopic model provides the opportunity to exploit robust Wnt regulated gene expression in a more responsive microenvironment than can be achieved in cell culture and simple flank xenograft models.
Here we propose a series of thoughts and comments that, if addressed, would in our opinion improve the study and its description.
1) We wonder why a xenograft model is necessary to induce a robust WNT response in these cells.
The authors describe this set-up as a strength, as it is supposed to provide physiological relevance, yet it is not clear to us why this is the case.
We welcome the opportunity to expand on our choice of an orthotopic xenograft model. It has been long established that cancer cells behave differently in different in vivo locations (Killion et al., 1998). Building on this, we confirmed this in our system that identical pancreatic cancer cells treated with the same PORCN inhibitor had very different responses in vitro, in the flank and in their orthotopic environment (Madan et al., 2018). To quote from our prior paper, “Looking only at genes decreasing more than 1.5-fold at 56 hours, we would have missed 817/1867 (44%) genes using a subcutaneous or 939/1867 (50%) using an in vitro model. Thus, the overall response to Wnt inhibition was reduced in the subcutaneous model and further blunted in vitro. An orthotopic model more accurately represents real biology.
The reason for this is presumably the very different orthotopic microenvironment, including tissue appropriate stroma-tumor, vascular-tumor, lymphatic-tumor, and humoral interactions.
Moreover, as the authors homogenize the tumour to perform bulk RNA-seq, we wonder whether they are not only sequencing mRNA from the cancer cells but also from infiltrating immune cells and/or from the surrounding connective tissue.
In experiments generating RNA-seq data from xenograft models, the resulting sequences can originate from either human (graft) or mouse (host). In order to account for this, following standard practice, we filtered reads prior to alignment using Xenome (Conway et al., 2012). We have added additional text to the methods to highlight this step in our pipeline.
2) If, as the established view implies, Wnt/beta-catenin only leads to gene activation, pathway
inhibition would free up the transcriptional machinery - there is evidence that some of its constituents are rate-limiting. The free machinery could now activate some other genes: the net effect observed would be their increased transcription upon Wnt inhibition, irrespective of beta-catenin's presence. Could this be considered as an alternative explanation for the genes that go up in both control and bcat4A lines upon ETC-159 administration? This, we think, is in part corroborated by the absence of enrichment of biological pathways in this group of genes. The genes that are beta-catenin-dependent and downregulated (D&R) are obviously not affected by this alternative explanation.
This is an interesting suggestion, and we will incorporate this thought into our discussion of potential mechanisms.
3) The authors mention that HPAF-II are Wnt addicted. Do they die upon ETC-159 administration, and is this effect rescued by exogenous WNT addition?
We and several others have previously reported that Wnt-addicted cells differentiate and/or senesce upon Wnt withdrawal in vivo but not in vitro. This is related to the broader changes in gene expression in the orthotopic tumors. The effect of PORCN inhibition has been demonstrated by us and others and is rescued by Wnt addition, downstream activation of Wnt signaling by e.g. APC mutation, and, as we show here, stabilized β-catenin.
4) Line 120: the authors write about Figure 1C: "This demonstrates that the growth of β-cat4A cells in vitro largely requires Wnts to activate β-catenin signaling." The opposite is true: control cells require WNT and form less colony with ETC159, while β-cat4A are independent from Wnt secretion.
We appreciate the reviewer pointing out our mis-statement. This error has now been corrected in the revised manuscript.
5) Lines 226-229: "The β-catenin independent repressed genes were notably enriched for motifs bound by homeobox factors including GSC2, POU6F2, and MSGN1. This finding aligns with the known role of non-canonical Wnt signaling in embryonic development" This statement assumes that target genes, or at least the beta-catenin independent ones, are conserved across tissues, including developing organs. This contrasts with the view that target genes in addition to the usual suspects (e.g., AXIN2, SP5 etc.) are modulated tissue-specifically - a view that the authors (and in fact, these reviewers) appear to support in their introduction.
We agree with the reviewer that a majority of Wnt-regulated genes are tissue specific. Indeed, the β-catenin independent Wnt-repressed genes may also be tissue specific. In other tissues, we speculate that other β-catenin independent Wnt-repressed genes may also have homeobox factor binding sites as well and so the general concept remains valid. We do not have sufficient data in other tissues to resolve this issue.
7) The luciferase and mutagenesis work presented in Figure 5 are crystal-clear. One important aspect that remains to be clarified is whether beta-catenin and/or TCF7L2 directly bind to the NRE sites. Or do the authors hypothesize that another factor binds here? We suggest the authors to show TCF7L2 binding tracks at the NRE/WRE motifs in the main figures.
A major question of the reviewers was, can we provide additional evidence that the NRE is bound by LEF/TCF family members. Our initial analysis of more datasets indicates TCF7L2 peaks are enriched on NREs in Wnt-β-catenin responsive cell lines like HCT116 and PANC1. These analyses appear to further support the model that the NRE binds TCF7L2, but we fully agree these analyses can neither prove nor disprove the model.
In our revision, we will analyze additional cut and run datasets as suggested and look at the HEPG2 datasets suggested by reviewer 1. We are concerned about tissue specificity as some of the genes are not expressed in e.g. HEPG2 or HEK293 cells where datasets are available. However, our data continues to support a functional role for the NRE in the modulation of β-catenin regulated genes. The best analysis would be more ChIP-Seq or Cut and Run assays on tissues, not cells, but these studies are beyond what we can do.
What about other TCF/LEFs and beta-catenin? Are there relevant datasets that could be explored to test whether all these bind here during Wnt activation?
As above, We will analyze additional ChIP and Cut & Run datasets to address this question looking at β-catenin and other LEF/TCF family members. We also reflect on the fact that ChIP-Seq does not necessarily imply that the targeted factor (e.g.,TCF7L2) is bound in the target site in all the cells.
The repression might be mediated by beta-catenin partnering with other factors that bind the NRE even by competing with TCF7L2.
We appreciate the insightful comments and now incorporate this into our discussion.
8) In general, while we greatly appreciate the github page to replicate the analysis, we feel that the methods' description is lacking, both concerning analytical details (e.g., the cutoff used for MACS2 peak calling) or basic experimental planning (e.g, how the luciferase assays were performed).
We thank reviewers for the suggestions and will add further details regarding the analysis
and experimental planning in the method sections.
9) The paper might benefit from the addition of quality metrics on the RNA-seq. Interesting for example would be to see a PCA analysis - as a more unbiased approach - rather than the kmeans clustering.
We have this data and will add it to the revised manuscript.
10) It seems that in Figure 3A the clusters are mislabelled as compared to Figure 3B and Figure 1. Here the repressor clusters are labelled DR5, DR6 and DN7 whereas in the rest of the paper they are labelled DR1, DR2 and DN1.
Thank you for pointing out this issue. This has now been corrected in Figure 3.
11) The siCTNNB1 in Figure 5E is described to be a significant effect in the text whereas in Figure 5E this has a p value of 0.075.
Thank you for pointing out the p value did not cross the 0.05 threshold. We have modified the text to remove the word ‘significant’.
12) Line 396: 'Here we confirm and extend the identification of a TCF-dependent negative regulatory element (NRE), where beta-catenin interacts with TCF to repress gene expression'. We suggest caution in stating that beta-catenin and TCF directly repress gene expression by binding to NRE. In the current state the authors do not show that TCF & beta-catenin bind to these elements. See our previous point 7.
We appreciate the suggestion of the reviewers. We will be more cautious in our interpretation.
Further suggestions - or food for thoughts:
13) A frequently asked question in the field concerns the off-target effects of CHIR treatment as opposed to exposure to WNT ligands. CHIR treatment - in parallel to bcat4A overexpression - would allow the authors to delineate WNT independent effects of CHIR treatment and settle this debate.
We thank the reviewers for suggesting this interesting experiment to sort out the non- Wnt effects of GSK3 inhibition. Such a study would require a new set of animal experiments and a different analysis; we think this is beyond the scope of this manuscript.
14) We think that Figure 4C could be strengthened by adding more public TCF-related datasets (e.g., from ENCODE) to confirm the observation across datasets from different laboratories. In particular, the HEPG2 could possibly be improved as there is an excellent TCF7L2 dataset available by ENCODE.
Many more datasets are easily searchable through: https://www.factorbook.org/.
As above, we will analyze the HEPG2 dataset. We plan on updating Fig 4 with data from analysis from different datasets such as (Blauwkamp et al., 2008; Zambanini et al., 2022).
15) The authors show that there is no specific spacing between NREs and WREs. This implies that it is not likely that TCF7L2 recognizes both at the same time through the C-clamp. Do the authors think that there might be a pattern discernible when comparing the location of WRE and NRE in relation to the TCF7L2 ChIP-seq peak summit? This would allow inferring whether TCF7L2 more likely directly binds the WRE (presumably) and if the NRE is bound by a cofactor.
This is an interesting suggestion and we will conduct this analysis as suggested on available datasets (as the result may be different in different tissue types with varying degrees of Wnt/β-catenin signaling).
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Overall, the study provides a solid framework for understanding noncanonical transcriptional ____outputs of Wnt signaling in a cancer context. The majority of the conclusions are well supported by the data. However, there are a few substantive points that require clarification before the manuscript is ready for publication.
Major Comments
The authors' central claim-that their findings represent a comprehensive analysis of the β-catenin- independent arm of Wnt signaling and uncover a "cis-regulatory grammar" governing Wnt-dependent gene activation versus repression-is overstated based on the presented data.
We appreciate the reviewers concern and will temper our language.
Specifically:
• Figure 3B identifies TF-binding motifs enriched among different Wnt-responsive gene clusters, but the authors only functionally investigate the role of NRE in β-catenin-dependent repression, particularly in the context of TCF motif interaction.
• To support a broader claim regarding cis-regulatory grammar, additional analyses are required:
o What is the distribution of NREs across all clusters? Are they exclusive to β-catenin-dependent repressed clusters, or more broadly present?
The distribution of the NREs is a statistically significant enrichment; they are observed in the repressed clusters more frequently than expected by chance alone, but they are present elsewhere as well. We have tempered our language around the cis-regulatory grammar.
o Do NREs interact with other enriched motifs beyond TCF? Is this interaction specific to repression or also involved in activation?
This is an interesting question beyond the scope of this analysis. Our dataset uses multiple interventions; The NREs may interact with other motifs but we would need more transcriptional analysis data with biological intervention to assess this.
o A more comprehensive analysis of cis-element combinations is needed to draw conclusions about their collective influence on gene regulation across clusters.
We agree; This would be a great question if we had TCF binding data in our orthotopic xenograft model. It’s a dataset we do not have, nor do we have the resources to pursue this.
Other important clarifications:
• The use of the term "wild-type" to describe HPAF-II cells is potentially misleading. These cells are not genetically wild-type and harbor multiple oncogenic alterations.
Thank you for pointing this out. We will use the word “parental” in the text
• The manuscript does not clearly present the kinetics of Wnt target downregulation upon ETC-159 treatment of HPAF-II cells. Understanding whether repression mirrors activation dynamics (e.g., delay or persistence of Wnt effects) is essential to interpreting the system's temporal behavior.
We previously addressed the temporal dynamics of activation and repression in our more comprehensive time course papers (Harmston et al., 2020; Madan et al., 2018); there are differences in the dynamics that are difficult to tease out in this new dataset as the density of time points is less. Having said that, we will compare the time course and annotate the sets of genes identified in this current study with the data from our original study to provide more information on the temporal dynamics of this system.
Minor Comment
• The statement in Figure 1C (lines 119-120) that "growth of β-cat4A cells in vitro largely requires Wnts to activate β-catenin signaling" is inconsistent with the data. As the β-cat4A allele encodes a constitutively active form of β-catenin, Wnts should not be required. Please revise this conclusion for clarity.
We thank the reviewers for pointing out this mis-statement. We have corrected this.
Reviewer #2 (Significance (Required)):
This study offers a systematic classification of Wnt-responsive gene expression dynamics, differentiating between β-catenin-dependent and -independent mechanisms. The insights into temporal expression patterns and the potential role of the NRE element in transcriptional repression add depth to our understanding of Wnt signaling. These findings have relevance for developmental biology, stem cell biology, and cancer research-particularly in understanding how Wnt-mediated repression may influence tumor progression and therapeutic response.
Nice review; thank you.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
… The work advances understanding of Wnt mediated repression via cis regulatory grammar.
Major Concerns
1) Statistical thresholds and clustering - The criteria for classifying β catenin-dependent versus - independent genes rely on FDR cutoffs above or below 0.1. If the more stringent cutoff of 0.05 was used, how many genes would still be considered Wnt regulated?
We can readily address this in a revised manuscript.
2) Validation of selected β catenin-dependent and -independent Wnt target genes - While the authors identify β catenin-dependent and -independent Wnt target genes (4 selected genes from different clusters in Fig.2), RT-qPCR based validation of Axin2 has been performed in Fig. S3. Authors should also validate other 3 genes as well.
We had considered performing qPCR to re-validate some of our gene-expression changes but qPCR analyses is intrinsically more error prone than RNAseq, and we believe the literature shows that qPCR from the same samples will not add any extra utility. Previous studies that have examined this question have reported excellent correlation between the RNAseq and pPCR (Asmann et al., 2009; Griffith et al., 2010; Wu et al., 2014).
3) NRE mechanistic insight - The most important contribution of this manuscript is the extension of the importance of the NRE motif in Wnt regulated enhancers. But the mutagenesis data provided is insufficient to conclusively nail down that the NREs are responsible for the repression. The effects in the synthetic reporters in Fig. 4D are small - it's not clear that there is much activity in the MimRep to be repressed by the NREs. The data in Fig. 5 is a better context to test the importance of the NREs, but the authors use deletion analysis which is too imprecise and settle for single nucleotide mutants in individual NREs in the ABHD11-AS1 reporter. In the Axin2 report, they mutate sequences outside of the NRE. It's too inconsistent. They should mutate 3 or 4 positions within the NRE in BOTH motifs in the context of the ABHD11-AS1 reporter. Same for the Axin2 reporter.
We feel our analysis, coupled with the Kim paper (Kim et al., 2017), support the role of the NRE. We agree that more data is always desirable, but in our current circumstances are we cannot add additional wetlab experiments.
Regarding Figure 4D, this is a synthetic system lacking the endogenous elements in the promoter. We agree with the reviewer that the effect is small but we would also like to point out that adding the well-established 2WRE in front of the MinRep increased the transcription activity to 1.5 fold, which is of similar magnitude change of the 2NRE deceasing the transcriptional activity 1/1.5 = 0.6.
In Kim et al, it was shown that mutating the 11st nucleotide of the NRE motif showed the strongest effect, so we followed their lead in only mutated the 11st nucleotide in ABHD11- AS1 NRE.
As for the putative NRE sequence present in AXIN2 promoter, its downstream sequence is polyT (__GTGTTTTTTTT__TTTTTTTTTT), if we only mutate 11st nucleotide to G/C, we could create similar sequence to NRE, so we mutated sequences outside of the NRE to fully disrupt it.
4) Even if the mutagenesis is done more completely, the results simply replicate that of the Goentoro group. In Kim et al 2017, they provide suggestive (not convincing) evidence that TCFs directly bind to the NRE. The authors of this manuscript should explore that in more detail, e.g., can purified TCF bind to the NRE sequence? Can the authors design experiments to directly test whether beta-catenin is acting through the NRE - their data currently only demonstrates that the NRE provide a negative input to the reporters - that's an important mechanistic difference.
We point out that our minimal reporter studies with the NRE showed a repressive effect in HCT116 (colorectal cancer cells with stabilized β-catenin) but not HT1080 (sarcoma cells with low Wnt) supporting the importance of β-catenin acting through the NRE (Figs. 4D, 4E).
We fully agree with the reviewers that additional study of TCF interaction with the NRE would be of value. While EMSA and culture-based ChIP assays would be of some value, the best study should be done in vivo where the system is most robust. We are not in a position to do these studies, but we will add in a discussion of this as a limitation of the current study.
5) In vertebrates, some TCFs are more repressive than others and TLEs have been implicated in repressive. Exploring these factors in the context of the NRE would increase the value of this story.
This is an interesting idea but beyond the scope of the current manuscript. It is likely this would be dependent on tissue specific expression, local expression levels, and local binding of co-factors. As we look at other TCF members in other datasets we may be able to address this. Further wetlab experiments are beyond the scope of this work.
**Referees cross-commenting**
I respectfully disagree that the luciferase assays are sufficient. Using deletion analysis to understand the function of specific binding sites is insufficient and the more specific mutations of NREs are incomplete. Regarding this paper extending our knowledge of direct transcriptional repression by Wnt/bcat signaling, I don't agree that it adds much - there are numerous datasets where Wnt signaling activates and represses genes - the trick is determining whether any of the repressed genes are the result and direct regulation by TCF/bcat. They don't explore that. The main finding is an extension of the work by Lea Goentoro on the importance of the NRE motif, but they don't address whether TCF directly associates with this sequence. Goentoro argued in the 2017 paper that it does, but that data is unconvincing to me. Can purified TCF bind the NRE? Without that information (done carefully) this manuscript is very limited.
We respectfully disagree with the reviewer regarding the contribution of this manuscript. There are certainly many datasets looking at Wnt-regulated genes in tissue culture, but these cell-based studies are underpowered to really understand Wnt biology. There are only two papers, ours and Cantú’s, that address Wnt repressed genes in any depth. No prior papers have differentiated β-catenin dependent from β-catenin independent genes before, and certainly not in an orthotopic animal model.
A major impact of our study is the finding that only 10% of Wnt regulated genes are independent of β-catenin, at least in pancreatic cancer. We feel this is a major contribution. We further add to this analysis by re-enforcing/extend the prior evidence on the NRE in humans (and correct the motif sequence!) for Wnt-repressed genes. Our data supports the fine-tuning of the Wnt/β-catenin regulated genes by a cis-regulatory grammar.
Reviewer #3 (Significance (Required)):
Overall, this study advances our understanding of the dual roles of Wnt signaling in gene activation and repression, highlighting the role of the NRE motif. But this is an extension of the original NRE paper (Kim et al 2017) with no mechanistic advance beyond that original work. The transcriptomics in the first part of the manuscript have some value, but similar data sets already exist.
We respectfully but strongly disagree with the reviewer. First, our work examines the NRE in a large-scale in vivo transcriptome dataset, significantly extending the candidate gene approach of Kim et al. Secondly, we disagree with the comment that “similar data sets already exist.” Indeed, reviewer 1 (C. Cantú) specifically pointed out we had addressed an “yet-unsolved question in the field” on whether and how β-catenin repressed genes.
__3. __Description of the revisions that have already been incorporated in the transferred manuscript
To date we have only corrected several typographical errors.
- Description of analyses that authors prefer not to carry out
We fully agree with the reviewers that additional study of TCF interaction with the NRE would be of value. While EMSA and cell culture-based ChIP assays would be of some modest value, they have already been done in vitro by Kim et al. (Kim et al., 2017) and the best next study should be done in vivo in Wnt-responsive cancers or tissues where the biology is most robust (Madan et al., 2018) . We are not in a position to do these studies, but we will add this into the discussion as a limitation of the current study. We also acknowledge that the NRE may interact with other currently unidentified factors.
Reviewer 1 asked about considering experiments to determine non-Wnt effects of GSK3 inhibitors like CHIR. Such a study, while interesting, would require a new set of animal experiments and a different analysis; we think this is beyond the scope of this manuscript.
Finally, we note that the Virshup lab at Duke-NUS Medical School in Singapore, where these in vivo studies were performed, has closed as of July 1, 2025 and the various lab members have moved on to new adventures. Because of this, we are unable to undertake new wet-lab studies.
Thank you for your consideration,
For the authors,
David Virshup
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
PAPS is required for all sulfotransferase reactions in which a sulfate group is covalently attached to amino acid residues of proteins or to side chains of proteoglycans. This sulfation is crucial for properly organizing the apical extracellular matrix (aECM) and expanding the lumen in the Drosophila salivary gland. Loss of Papss potentially leads to decreased sulfation, disorganizing the aECM, and defects in lumen formation. In addition, Papss loss destabilizes the Golgi structures.
In Papss mutants, several changes occur in the salivary gland lumen of Drosophila. The tube lumen is very thin and shows irregular apical protrusions. There is a disorganization of the apical membrane and a compaction of the apical extracellular matrix (aECM). The Golgi structures and intracellular transport are disturbed. In addition, the ZP domain proteins Piopio (Pio) and Dumpy (Dpy) lose their normal distribution in the lumen, which leads to condensation and dissociation of the Dpy-positive aECM structure from the apical membrane. This results in a thin and irregularly dilated lumen.
- The authors describe various changes in the lumen in mutants, from thin lumen to irregular expansion. I would like to know the correct lumen diameter, and length, besides the total area, by which one can recognize thin and irregular.
We have included quantification of the length and diameter of the salivary gland lumen in the stage 16 salivary glands of control, Papss mutant, and salivary gland-specific rescue embryos (Figure 1J, K). As described, Papss mutant embryos have two distinct phenotypes, one group with a thin lumen along the entire lumen and the other group with irregular lumen shapes. Therefore, we separated the two groups for quantification of lumen diameter. Additionally, we have analyzed the degree of variability for the lumen diameter to better capture the range of phenotypes observed (Figure 1K'). These quantifications enable a more precise assessment of lumen morphology, allowing readers to distinguish between thin and irregular lumen phenotypes.
The rescue is about 30%, which is not as good as expected. Maybe the wrong isoform was taken. Is it possible to find out which isoform is expressed in the salivary glands, e.g., by RNA in situ Hyb? This could then be used to analyze a more focused rescue beyond the paper.
Thank you for this point, but we do not agree that the rescue is about 30%. In Papss mutants, about 50% of the embryos show the thin lumen phenotype whereas the other 50% show irregular lumen shapes. In the rescue embryos with a WT Papss, few embryos showed thin lumen phenotypes. About 40% of the rescue embryos showed "normal, fully expanded" lumen shapes, and the remaining 60% showed either irregular (thin+expanded) or slightly overexpanded lumen. It is not uncommon that rescue with the Gal4/UAS system results in a partial rescue because it is often not easy to achieve the balance of the proper amount of the protein with the overexpression system.
To address the possibility that the wrong isoform was used, we performed in situ hybridization to examine the expression of different Papss spice forms in the salivary gland. We used probes that detect subsets of splice forms: A/B/C/F/G, D/H, and E/F/H, and found that all probes showed expression in the salivary gland, with varying intensities. The original probe, which detects all splice forms, showed the strongest signals in the salivary gland compared to the new probes which detect only a subset. However, the difference in the signal intensity may be due to the longer length of the original probe (>800 bp) compared to other probes that were made with much smaller regions (~200 bp). Digoxigenin in the DIG labeling kit for mRNA detection labels the uridine nucleotide in the transcript, and the probes with weaker signals contain fewer uridines (all: 147; ABCFG, 29; D, 36; EFH, 66). We also used the Papss-PD isoform, for a salivary gland-specific rescue experiment and obtained similar results to those with Papss-PE (Figure 1I-L, Figure 4D and E).
Furthermore, we performed additional experiments to validate our findings. We performed a rescue experiment with a mutant form of Papss that has mutations in the critical rescues of the catalytic domains of the enzyme, which failed to rescue any phenotypes, including the thin lumen phenotype (Figure 1H, J-L), the number and intensity of WGA puncta (Figure 3I, I'), and cell death (Figure 4D, E). These results provide strong evidence that the defects observed in Papss mutants are due to the lack of sulfation.
Crb is a transmembrane protein on the apicolateral side of the membrane. Accordingly, the apicolateral distribution can be seen in the control and the mutant. I believe there are no apparent differences here, not even in the amount of expression. However, the view of the cells (frame) shows possible differences. To be sure, a more in-depth analysis of the images is required. Confocal Z-stack images, with 3D visualization and orthogonal projections to analyze the membranes showing Crb staining together with a suitable membrane marker (e.g. SAS or Uif). This is the only way to show whether Crb is incorrectly distributed. Statistics of several papas mutants would also be desirable and not just a single representative image. When do the observed changes in Crb distribution occur in the development of the tubes, only during stage 16? Is papss only involved in the maintenance of the apical membrane? This is particularly important when considering the SJ and AJ, because the latter show no change in the mutants.
We appreciate your suggestion to more thoroughly analyze Crb distribution. We adapted a method from a previous study (Olivares-Castiñeira and Llimargas, 2017) to quantify Crb signals in the subapical region and apical free region of salivary gland cells. Using E-Cad signals as a reference, we marked the apical cell boundaries of individual cells and calculated the intensity of Crb signals in the subapical region (along the cell membrane) and in the apical free region. We focused on the expanded region of the SG lumen in Papss mutants for quantification, as the thin lumen region was challenging to analyze. This quantification is included in Figure 2D. Statistical analysis shows that Crb signals were more dispersed in SG cells in Papss mutants compared to WT.
A change in the ECM is only inferred based on the WGA localization. This is too few to make a clear statement. WGA is only an indirect marker of the cell surface and glycosylated proteins, but it does not indicate whether the ECM is altered in its composition and expression. Other important factors are missing here. In addition, only a single observation is shown, and statistics are missing.
We understand your concern that WGA localization alone may not be sufficient to conclude changes in the ECM. However, we observed that luminal WGA signals colocalize with Dpy-YFP in the WT SG (Figure 5-figure supplement 2C), suggesting that WGA detects the aECM structure containing Dpy. The similar behavior of WGA and Dpy-YFP signals in multiple genotypes further supports this idea. In Papss mutants with a thin lumen phenotype, both WGA and Dpy-YFP signals are condensed (Figure 5E-H), and in pio mutants, both are absent from the lumen (Figure 6B, D). We analyzed WGA signals in over 25 samples of WT and Papss mutants, observing consistent phenotypes. We have included the number of samples in the text. While we acknowledge that WGA is an indirect marker, our data suggest that it is a reliable indicator of the aECM structure containing Dpy.
Reduced WGA staining is seen in papss mutants, but this could be due to other circumstances. To be sure, a statistic with the number of dots must be shown, as well as an intensity blot on several independent samples. The images are from single confocal sections. It could be that the dots appear in a different Z-plane. Therefore, a 3D visualization of the voxels must be shown to identify and, at best, quantify the dots in the organ.
We have quantified cytoplasmic punctate WGA signals. Using spinning disk microscopy with super-resolution technology (Olympus SpinSR10 Sora), we obtained high-resolution images of cytoplasmic punctate signals of WGA in WT, Papss mutant, and rescue SGs with the WT and mutant forms of Papss-PD. We then generated 3D reconstructed images of these signals using Imaris software (Figure 3E-H) and quantified the number and intensity of puncta. Statistical analysis of these data confirms the reduction of the number and intensity of WGA puncta in Papss mutants (Figure 3I, I'). The number of WGA puncta was restored by expressing WT Papss but not the mutant form. By using 3D visualization and quantification, we have ensured that our results are not limited to a single confocal section and account for potential variations in Z-plane localization of the dots.
A colocalization analysis (statistics) should be shown for the overlap of WGA with ManII-GFP.
Since WGA labels multiple structures, including the nuclear envelope and ECM structures, we focused on assessing the colocalization of the cytoplasmic WGA punctate signals and ManII-GFP signals. Standard colocalization analysis methods, such as Pearson's correlation coefficient or Mander's overlap coefficient, would be confounded by WGA signals in other tissues. Therefore, we used a fluorescent intensity line profile to examine the spatial relationship between WGA and ManII-GFP signals in WT and Papss mutants (Figure 3L, L').
I do not understand how the authors describe "statistics of secretory vesicles" as an axis in Figure 3p. The TEM images do not show labeled secretory vesicles but empty structures that could be vesicles.
Previous studies have analyzed "filled" electron-dense secretory vesicles in TEM images of SG cells (Myat and Andrew, 2002, Cell; Fox et al., 2010, J Cell Biol; Chung and Andrew, 2014, Development). Consistent with these studies, our WT TEM images show these vesicles. In contrast, Papss mutants show a mix of filled and empty structures. For quantification, we specifically counted the filled electron-dense vesicles (now Figure 3W). A clear description of our analysis is provided in the figure legend.
- The quality of the presented TEM images is too low to judge any difference between control and mutants. Therefore, the supplement must present them in better detail (higher pixel number?).
We disagree that the quality of the presented TEM images is too low. Our TEM images have sufficient resolution to reveal details of many subcellular structures, such as mitochondrial cisternae. The pdf file of the original submission may not have been high resolution. To address this concern, we have provided several original high-quality TEM images of both WT and Papss mutants at various magnifications in Figure 2-figure supplement 2. Additionally, we have included low-magnification TEM images of WT and Papss mutants in Figure 2H and I to provide a clearer view of the overall SG lumen morphology.
Line 266: the conclusion that apical trafficking is "significantly impaired" does not hold. This implies that Papss is essential for apical trafficking, but the analyzed ECM proteins (Pio, Dumpy) are found apically enriched in the mutants, and Dumpy is even secreted. Moreover, they analyze only one marker, Sec15, and don't provide data about the quantification of the secretion of proteins.
We agree and have revised our statement to "defective sulfation affects Golgi structures and multiple routes of intracellular trafficking".
DCP-1 was used to detect apoptosis in the glands to analyze acellular regions. However, the authors compare ST16 control with ST15 mutant salivary glands, which is problematic. Further, it is not commented on how many embryos were analyzed and how often they detect the dying cells in control and mutant embryos. This part must be improved.
Thank you for the comment. We agree and have included quantification. We used stage 16 samples from WT and Papss mutants to quantify acellular regions. Since DCP-1 signals are only present at a specific stage of apoptosis, some acellular regions do not show DCP-1 signals. Therefore, we counted acellular regions regardless of DCP-1 signals. We also quantified this in rescue embryos with WT and mutant forms of Papss, which show complete rescue with WT and no rescue with the mutant form, respectively. The graph with a statistical analysis is included (Figure 4D, E).
WGA and Dumpy show similar condensed patterns within the tube lumen. The authors show that dumpy is enriched from stage 14 onwards. How is it with WGA? Does it show the same pattern from stage 14 to 16? Papss mutants can suffer from a developmental delay in organizing the ECM or lack of internalization of luminal proteins during/after tube expansion, which is the case in the trachea.
Dpy-YFP and WGA show overlapping signals in the SG lumen throughout morphogenesis. Dpy-YFP is SG enriched in the lumen from stage 11, not stage 14 (Figure 5-figure supplement 2). WGA is also detected in the lumen throughout SG morphogenesis, similar to Dpy. In the original supplemental figure, only a stage 16 SG image was shown for co-localization of Dpy-YFP and WGA signals in the SG lumen. We have now included images from stage 14 and 15 in Figure 5-figure supplement 2C.
Given that luminal Pio signals are lost at stage 16 only and that Dpy signals appear as condensed structures in the lumen of Papss mutants, it suggests that the internalization of luminal proteins is not impaired in Papss mutants. Rather, these proteins are secreted but fail to organize properly.
Line 366. Luminal morphology is characterized by bulging and constrictions. In the trachea, bulges indicate the deformation of the apical membrane and the detachment from the aECM. I can see constrictions and the collapsed tube lumen in Fig. 6C, but I don't find the bulges of the apical membrane in pio and Np mutants. Maybe showing it more clearly and with better quality will be helpful.
Since the bulging phenotype appears to vary from sample to sample, we have revised the description of the phenotype to "constrictions" to more accurately reflect the consistent observations. We quantified the number of constrictions along the entire lumen in pio and Np mutants and included the graph in Figure 6F.
The authors state that Papss controls luminal secretion of Pio and Dumpy, as they observe reduced luminal staining of both in papss mutants. However, the mCh-Pio and Dumpy-YFP are secreted towards the lumen. Does papss overexpression change Pio and Dumpy secretion towards the lumen, and could this be another explanation for the multiple phenotypes?
Thank you for the comment. To clarify, we did not observe reduced luminal staining of Pio and Dpy in Papss mutants, nor did we state that Papss controls luminal secretion of Pio and Dpy. In Papss mutants, Pio luminal signals are absent specifically at stage 16 (Figure 5H), whereas strong luminal Pio signals are present until stage 15 (Figure 5G). For Dpy-YFP, the signals are not reduced but condensed in Papss mutants from stages 14-16 (Figure 5D, H).
It remains unclear whether the apparent loss of Pio signals is due to a loss of Pio protein in the lumen or due to epitope masking resulting from protein aggregation or condensation. As noted in our response to Comment 11 internalization of luminal proteins seems unaffected in Papss mutants; proteins like Pio and Dpy are secreted into the lumen but fail to properly organize. Therefore, we have not tested whether Papss overexpression alters the secretion of Pio or Dpy.
In our original submission, we incorrectly stated that uniform luminal mCh-Pio signals were unchanged in Papss mutants. Upon closer examination, we found these signals are absent in the expanded luminal region in stage 16 SG (where Dpy-YFP is also absent), and weak mCh-Pio signals colocalize with the condensed Dpy-YFP signals (Figure 5C, D). We have revised the text accordingly.
Regulation of luminal ZP protein level is essential to modulate the tube expansion; therefore, Np releases Pio and Dumpy in a controlled manner during st15/16. Thus, the analysis of Pio and Dumpy in NP overexpression embryos will be critical to this manuscript to understand more about the control of luminal ZP matrix proteins.
Thanks for the insightful suggestion. We overexpressed both the WT and mutant form of Np using UAS-Np.WT and UAS-Np.S990A lines (Drees et al., 2019) and analyzed mCh-Pio, Pio antibody, and Dpy-YFP signals. It is important to note that these overexpression experiments were done in the presence of the endogenous WT Np.
Overexpression of Np.WT led to increased levels of mCh-Pio, Pio, and Dpy-YFP signals in the lumen and at the apical membrane. In contrast, overexpression of Np.S990A resulted in a near complete loss of luminal mCh-Pio signals. Pio antibody signals remained strong at the apical membrane but was weaker in the luminal filamentous structures compared to WT.
Due to the GFP tag present in the UAS-Np.S990A line, we could not reliably analyze Dpy-YFP signals because of overlapping fluorescent signals in the same channel. However, the filamentous Pio signals in the lumen co-localized with GFP signals, suggesting that these structures might also include Dpy-YFP, although this cannot be confirmed definitively.
These results suggest that overexpressed Np.S990A may act in a dominant-negative manner, competing with endogenous Np and impairing proper cleavage of Pio (and mCh-Pio). Nevertheless, some level of cleavage by endogenous Np still appears to occur, as indicated by the residual luminal filamentous Pio signals. These new findings have been incorporated into the revised manuscript and are shown in Figure 6H and 6I.
Minor: Fig. 5 C': mChe-Pio and Dumpy-YFP are mixed up at the top of the images.
Thanks for catching this error. It has been corrected.
Sup. Fig7. A shows Pio in purple but B in green. Please indicate it correctly.
It has been corrected.
Reviewer #1 (Significance (Required)):
In 2023, the functions of Pio, Dumpy, and Np in the tracheal tubes of Drosophila were published. The study here shows similar results, with the difference that the salivary glands do not possess chitin, but the two ZP proteins Pio and Dumpy take over its function. It is, therefore, a significant and exciting extension of the known function of the three proteins to another tube system. In addition, the authors identify papss as a new protein and show its essential function in forming the luminal matrix in the salivary glands. Considering the high degree of conservation of these proteins in other species, the results presented are crucial for future analyses and will have further implications for tubular development, including humans.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Summary: There is growing appreciation for the important of luminal (apical) ECM in tube development, but such matrices are much less well understood than basal ECMs. Here the authors provide insights into the aECM that shapes the Drosophila salivary gland (SG) tube and the importance of PAPSS-dependent sulfation in its organization and function.
The first part of the paper focuses on careful phenotypic characterization of papss mutants, using multiple markers and TEM. This revealed reduced markers of sulfation (Alcian Blue staining) and defects in both apical and basal ECM organization, Golgi (but not ER) morphology, number and localization of other endosomal compartments, plus increased cell death. The authors focus on the fact that papss mutants have an irregular SG lumen diameter, with both narrowed regions and bulged regions. They address the pleiotropy, showing that preventing the cell death and resultant gaps in the tube did not rescue the SG luminal shape defects and discussing similarities and differences between the papss mutant phenotype and those caused by more general trafficking defects. The analysis uses a papss nonsense mutant from an EMS screen - I appreciate the rigorous approach the authors took to analyze transheterozygotes (as well as homozygotes) plus rescued animals in order to rule out effects of linked mutations.
The 2nd part of the paper focuses on the SG aECM, showing that Dpy and Pio ZP protein fusions localize abnormally in papss mutants and that these ZP mutants (and Np protease mutants) have similar SG lumen shaping defects to the papss mutants. A key conclusion is that SG lumen defects correlate with loss of a Pio+Dpy-dependent filamentous structure in the lumen. These data suggest that ZP protein misregulation could explain this part of the papss phenotype.
Overall, the text is very well written and clear. Figures are clearly labeled. The methods involve rigorous genetic approaches, microscopy, and quantifications/statistics and are documented appropriately. The findings are convincing, with just a few things about the fusions needing clarification.
minor comments 1. Although the Dpy and Qsm fusions are published reagents, it would still be helpful to mention whether the tags are C-terminal as suggested by the nomenclature, and whether Westerns have been performed, since (as discussed for Pio) cleavage could also affect the appearance of these fusions.
Thanks for the comment. Dpy-YFP is a knock-in line in which YFP is inserted into the middle of the dpy locus (Lye et al., 2014; the insertion site is available on Flybase). mCh-Qsm is also a knock-in line, with mCh inserted near the N-terminus of the qsm gene using phi-mediated recombination using the qsmMI07716 line (Chu and Hayashi, 2021; insertion site available on Flybase). Based on this, we have updated the nomenclature from Qsm-mCh to mCh-Qsm throughout the manuscript to accurately reflect the tag position. To our knowledge, no western blot has been performed on Dpy-YFP or mCh-Qsm lines. We have mentioned this explicitly in the Discussion.
The Dpy-YFP reagent is a non-functional fusion and therefore may not be a wholly reliable reporter of Dpy localization. There is no antibody confirmation. As other reagents are not available to my knowledge, this issue can be addressed with text acknowledgement of possible caveats.
Thanks for raising this important point. We have added a caveat in the Discussion noting this limitation and the need for additional tools, such as an antibody or a functional fusion protein, to confirm the localization of Dpy.
TEM was done by standard chemical fixation, which is fine for viewing intracellular organelles, but high pressure freezing probably would do a better job of preserving aECM structure, which looks fairly bad in Fig. 2G WT, without evidence of the filamentous structures seen by light microscopy. Nevertheless, the images are sufficient for showing the extreme disorganization of aECM in papss mutants.
We agree that HPF is a better method and intent to use the HPF system in future studies. We acknowledge that chemical fixation contributes to the appearance of a gap between the apical membrane and the aECM, which we did not observe in the HPF/FS method (Chung and Andrew, 2014). Despite this, the TEM images still clearly reveal that Papss mutants show a much thinner and more electron-dense aECM compared to WT (Figure 2H, I), consistent to the condensed WGA, Dpy, and Pio signals in our confocal analyses. As the reviewer mentioned, we believe that the current TEM data are sufficient to support the conclusion of severe aECM disorganization and Golgi defects in Papss mutants.
The authors may consider citing some of the work that has been done on sulfation in nematodes, e.g. as reviewed here: https://pubmed.ncbi.nlm.nih.gov/35223994/ Sulfation has been tied to multiple aspects of nematode aECM organization, though not specifically to ZP proteins.
Thank you for the suggestion. Pioneering studies in C. elegans have highlighted the key role of sulfation in diverse developmental processes, including neuronal organization, reproductive tissue development, and phenotypic plasticity. We have now cited several works.
Reviewer #2 (Significance (Required)):
This study will be of interest to researchers studying developmental morphogenesis in general and specifically tube biology or the aECM. It should be particularly of interest to those studying sulfation or ZP proteins (which are broadly present in aECMs across organisms, including humans).
This study adds to the literature demonstrating the importance of luminal matrix in shaping tubular organs and greatly advances understanding of the luminal matrix in the Drosophila salivary gland, an important model of tubular organ development and one that has key matrix differences (such as no chitin) compared to other highly studied Drosophila tubes like the trachea.
The detailed description of the defects resulting from papss loss suggests that there are multiple different sulfated targets, with a subset specifically relevant to aECM biology. A limitation is that specific sulfated substrates are not identified here (e.g. are these the ZP proteins themselves or other matrix glycoproteins or lipids?); therefore it's not clear how direct or indirect the effects of papss are on ZP proteins. However, this is clearly a direction for future work and does not detract from the excellent beginning made here.
My expertise: I am a developmental geneticist with interests in apical ECM
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
In this work Woodward et al focus on the apical extracellular matrix (aECM) in the tubular salivary gland (SG) of Drosophila. They provide new insights into the composition of this aECM, formed by ZP proteins, in particular Pio and Dumpy. They also describe the functional requirements of PAPSS, a critical enzyme involved in sulfation, in regulating the expansion of the lumen of the SG. A detailed cellular analysis of Papss mutants indicate defects in the apical membrane, the aECM and in Golgi organization. They also find that Papss control the proper organization of the Pio-Dpy matrix in the lumen. The work is well presented and the results are consistent.
Main comments
- This work provides a detailed description of the defects produced by the absence of Papss. In addition, it provides many interesting observations at the cellular and tissular level. However, this work lacks a clear connection between these observations and the role of sulfation. Thus, the mechanisms underlying the phenotypes observed are elusive. Efforts directed to strengthen this connection (ideally experimentally) would greatly increase the interest and relevance of this work.
Thank you for this thoughtful comment. To directly test whether the phenotypes observed in Papss mutants are due to the loss of sulfation activity, we generated transgenic lines expressing catalytically inactive forms of Papss, UAS-PapssK193A, F593P, in which key residues in the APS kinase and ATP sulfurylase domains are mutated. Unlike WT UAS-Papss (both the Papss-PD or Papss-PE isoforms), the catalytically inactive UAS-Papssmut failed to rescue any of the phenotypes, including the thin lumen phenotype (Figure 1I-L), altered WGA signals (Figure I, I') and the cell death phenotype (Figure 4D, E). These findings strongly support the conclusion that the enzymatic sulfation activity of Papss is essential for the developmental processes described in this study.
- A main issue that arises from this work is the role of Papss at the cellular level. The results presented convincingly indicate defects in Golgi organization in Papss mutants. Therefore, the defects observed could stem from general defects in the secretion pathway rather than from specific defects on sulfation. This could even underly general/catastrophic cellular defects and lead to cell death (as observed). This observation has different implications. Is this effect observed in SGs also observed in other cells in the embryo? If Papss has a general role in Golgi organization this would be expected, as Papss encodes the only PAPs synthatase in Drosophila. Can the authors test any other mutant that specifically affect Golgi organization and investigate whether this produces a similar phenotype to that of Papss?
Thank you for the comment. To address whether the defects observed in Papss mutants stem from general disruption of the secretory pathway due to Golgi disorganization, we examined mutants of two key Golgi components: Grasp65 and GM130.
In Grasp65 mutants, we observed significant defects in SG lumen morpholgy, including highly irregular SG lumen shape and multiple constrictions (100%; n=10/10). However, the lumen was not uniformly thin as in Papss mutants. In contrast, GM130 mutants-although this line was very sick and difficult to grow-showed relatively normal salivary glands morphology in the few embryos that survived to stage 16 (n=5/5). It is possible that only embryos with mild phenotypes progressed to this stages, limiting interpretation. These data have now been included in Figure 3-figure supplement 2. Overall, while Golgi disruption can affect SG morphology, the specific phenotypes seen in Papss mutants are not fully recapitulated by Grasp65 or GM130 loss.
- A model that conveys the different observations and that proposes a function for Papss in sulfation and Golgi organization (independent or interdependent?) would help to better present the proposed conclusions. In particular, the paper would be more informative if it proposed a mechanism or hypothesis of how sulfation affects SG lumen expansion. Is sulfation regulating a factor that in turn regulates Pio-Dpy matrix? Is it regulating Pio-Dpy directly? Is it regulating a product recognized by WGA? For instance, investigating Alcian blue or sulfotyrosine staining in pio, dpy mutants could help to understand whether Pio, Dpy are targets of sulfation.
Thank you for the comment. We're also very interested in learning whether the regulation of the Pio-Dpy matrix is a direct or indirect consequence of the loss of sulfation on these proteins. One possible scenario is that sulfation directly regulates the Pio-Dpy matrix by regulating protein stability through the formation of disulfide bonds between the conserved Cys residues responsible for ZP module polymerization. Additionally, the Dpy protein contains hundreds of EGF modules that are highly susceptible to O-glycosylation. Sulfation of the glycan groups attached to Dpy may be critical for its ability to form a filamentous structure. Without sulfation, the glycan groups on Dpy may not interact properly with the surrounding materials in the lumen, resulting in an aggregated and condensed structure. These possibilities are discussed in the Discussion.
We have not analyzed sulfation levels in pio or dpy mutants because sulfation levels in mutants of single ZP domain proteins may not provide much information. A substantial number of proteoglycans, glycoproteins, and proteins (with up to 1% of all tyrosine residues in an organism's proteins estimated to be sulfated) are modified by sulfation, so changes in sulfation levels in a single mutant may be subtle. Especially, the existing dpy mutant line is an insertion mutant of a transposable element; therefore, the sulfation sites would still remain in this mutant.
- Interpretation of Papss effects on Pio and Dpy would be desired. The results presented indicate loss of Pio antibody staining but normal presence of cherry-Pio. This is difficult to interpret. How are these results of Pio antibody and cherry-Pio correlating with the results in the trachea described recently (Drees et al. 2023)?
In our original submission, we stated that the uniform luminal mCh-Pio signals were not changed in Papss mutants, but after re-analysis, we found that these signals were actually absent from the expanded luminal region in stage 16 SG (where Dpy-YFP is also absent), and weak mCh-Pio signals colocalize with the condensed Dpy-YFP signals (Figure 5C, D). We have revised the text accordingly.
After cleavages by Np and furin, the Pio protein should have three fragments. The N-terminal region contains the N-terminal half of the ZP domain, and mCh-Pio signals show this fragment. The very C-terminal region should localize to the membrane as it contains the transmembrane domain. We think the middle piece, the C-terminal ZP domain, is recognized by the Pio antibody. The mCh-Pio and Pio antibody signals in the WT trachea (Drees et al., 2023) are similar to those in the SG. mCh-Pio signals are detected in the tracheal lumen as uniform signals, at the apical membrane, and in cytoplasmic puncta. Pio antibody signals are exclusively in the tracheal lumen and show more heterogenous filamentous signals.
In Papss mutants, the middle fragment (the C-terminal ZP domain) seems to be most affected because the Pio antibody signals are absent from the lumen. The loss of Pio antibody signals could be due to protein degradation or epitope masking caused by aECM condensation and protein misfolding. This fragment seems to be key for interacting with Dpy, since Pio antibody signals always colocalize with Dpy-YFP. The N-terminal mCh-Pio fragment does not appear to play a significant role in forming a complex with Dpy in WT (but still aggregated together in Papss mutants), and this can be tested in future studies.
In response to Reviewer 1's comment, we performed an additional experiment to test the role of Np in cleaving Pio to help organize the SG aECM. In this experiment, we overexpressed the WT and mutant form of Np using UAS-Np.WT and UAS-Np.S990A lines (Drees et al., 2019) and analyzed mCh-Pio, Pio antibody, and Dpy-YFP signals. Np.WT overexpression resulted in increased levels of mCh-Pio, Pio, and Dpy-YFP signals in the lumen and at the apical membrane. However, overexpression of Np.S990A resulted in the absence of luminal mCh-Pio signals. Pio antibody signals were strong at the apical membrane but rather weak in the luminal filamentous structures. Since the UAS-Np.S990A line has the GFP tag, we could not reliably analyze Dpy-YFP signals due to overlapping Np.S990A.GFP signals in the same channel. However, the luminal filamentous Pio signals co-localized with GFP signals, and we assume that these overlapping signals could be Dpy-YFP signals.
These results suggest that overexpressed Np.S990A may act in a dominant-negative manner, competing with endogenous Np and impairing proper cleavage of Pio (and mCh-Pio). Nevertheless, some level of cleavage by endogenous Np still appears to occur, as indicated by the residual luminal filamentous Pio signals. These new findings have been incorporated into the revised manuscript and are shown in Figure 6H and 6I.
A proposed model of the Pio-Dpy aECM in WT, Papss, pio, and Np mutants has now been included in Figure 7.
- What does the WGA staining in the lumen reveal? This staining seems to be affected differently in pio and dpy mutants: in pio mutants it disappears from the lumen (as dpy-YFP does), but in dpy mutants it seems to be maintained. How do the authors interpret these findings? How does the WGA matrix relate to sulfated products (using Alcian blue or sulfotyrosine)?
WGA binds to sialic acid and N-acetylglucosamine (GlcNAc) residues on glycoproteins and glycolipids. GlcNAc is a key component of the glycosaminoglycan (GAG) chains that are covalently attached to the core protein of a proteoglycan, which is abundant in the ECM. We think WGA detects GlcNAc residues in the components of the aECM, including Dpy as a core component, based on the following data. 1) WGA and Dpy colocalize in the lumen, both in WT (as thin filamentous structures) and Papss mutant background (as condensed rod-like structures), and 2) are absent in pio mutants. WGA signals are still present in a highly condensed form in dpy mutants. That's probably because the dpy mutant allele (dpyov1) has an insertion of a transposable element (blood element) into intron 11 and this insertion may have caused the Dpy protein to misfold and condense. We added the information about the dpy allele to the Results section and discussed it in the Discussion.
Minor points:
- The morphological phenotypic analysis of Papss mutants (homozygous and transheterozygous) is a bit confusing. The general defects are higher in Papss homozygous than in transheterozygotes over a deficiency. Maybe quantifying the defects in the heterozygote embryos in the Papss mutant collection could help to figure out whether these defects relate to Papss mutation.
We analyzed the morphology of heterozygous Papss mutant embryos. They were all normal. The data and quantifications have now been added to Figure 1-figure supplement 3.
- The conclusion that the apical membrane is affected in Papss mutants is not strongly supported by the results presented with the pattern of Crb (Fig 2). Further evidences should be provided. Maybe the TEM analysis could help to support this conclusion
We quantified Crb levels in the sub-apical and medial regions of the cell and included this new quantification in Figure 2D. TEM images showed variation in the irregularity of the apical membrane, even in WT, and we could not draw a solid conclusion from these images.
- It is difficult to understand why in Papss mutants the levels of WGA increase. Can the authors elaborate on this?
We think that when Dpy (and many other aECM components) are condensed and aggregated into the thin, rod-like structure in Papss mutants, the sugar residues attached to them must also be concentrated and shown as increased WGA signals.
- The explanation about why Pio antibody and mcherry-Pio show different patterns is not clear. If the antibody recognizes the C-t region, shouldn't it be clearly found at the membrane rather than the lumen?
The Pio protein is also cleaved by furin protease (Figure 5B). We think the Pio fragment recognized by the antibody should be a "C-terminal ZP domain", which is a middle piece after furin + Np cleavages.
- The qsm information does not seem to provide any relevant information to the aECM, or sulfation.
Since Qsm has been shown to bind to Dpy and remodel Dpy filaments in the muscle tendon (Chu and Hayashi, 2021), we believe that the different behavior of Qsm in the SG is still informative. As mentioned briefly in the Discussion, the cleaved Qsm fragment may localize differently, like Pio, and future work will need to test this. We have shortened the description of the Qsm localization in the manuscript and moved the details to the figure legend of Figure 5-figure supplement 3.
Reviewer #3 (Significance (Required)):
Previous reports already indicated a role for Papss in sulfation in SG (Zhu et al 2005). Now this work provides a more detailed description of the defects produced by the absence of Papss. In addition, it provides relevant data related to the nature and requirements of the aECM in the SG. Understanding the composition and requirements of aECM during organ formation is an important question. Therefore, this work may be relevant in the fields of cell biology and morphogenesis.
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Reviewer #2 (Public review):
Summary:
In the manuscript by Walter-McNeill, Kruglyak, and team, the authors provide solid evidence of another toxin-antidote (TA) system in C. elegans. Generally, TA systems involve selfish and linked genetic elements, one encoding a toxin that kills progeny inheriting it, unless an antidote (the second element) is also present. Currently, only two TA systems have been characterized in this species, pointing to the importance of identifying new instances of such systems to understand their transmission dynamics, prevalence, and functions in shaping worm populations.
Strengths:
This novel TA system (mll-1/smll-1) was identified on LGV in wild C. elegans isolates from the Hawaiian islands, by crossing divergent strains and observing allele frequency distortions by high-throughput genome sequencing after 10 generations. These allele frequency distortions were subsequently confirmed in another set of crosses with a separate divergent strain, and crosses of heterozygous males or hermaphrodites resulted in a pattern of L1 lethality in progeny (with a rod arrest phenotype) that suggested the maternal transmission of this TA system from the XZ1516 genetic background. By elegantly combining the use of near-isogenic lines, CRISPR editing to generate knock-outs, and a transgene rescue of the antidote gene, the authors identified the genes encoding the toxin and the antidote, which they refer to as mll-1 and smll-1. Moreover, the specific mll-1 isoform responsible for the production of the toxin was identified and mll-1 transcripts were observed by FISH in early and late embryos, as well as in larvae. Inducible expression of the toxin in various strains resulted in larval arrest and rod phenotypes. The authors then characterized the genetic variation of 550 wild isolates at the toxin/antidote region on LGV and distinguished three clades: (1) one with the conserved TA system, (2) one having lost the toxin and retaining a mostly functional antidote, and (3) one having lost the antidote and retaining a divergent yet coding toxin (this includes the reference strain Bristol N2, in which the homologous toxin gene has acquired mutations and is known as B0250.8). Further, the authors show that this region is under positive selection. These data are compelling and provide very strong evidence of a new TA system in this species.
Weaknesses:
The question remained as to how one clade, including N2, could retain the toxin gene but not possess a functional antidote. In the second part of the manuscript, the authors hypothesized that small RNA targeting (RNAi) of the toxin transcript could provide the necessary repression to allow worms to survive without the antidote. Through a meta-analysis of multiple small RNA datasets from the literature, the authors found evidence to support this idea, in which the toxin transcript is targeted by 22G siRNAs whose biogenesis is dependent on the Mutator foci protein, MUT-16. They note that from previous studies, mut-16 null mutants displayed a varied penetrance of larval arrest. In their own hands, mut-16 mutants displayed 15% varied larval arrest and 2% rod phenotypes. In an attempt to link B0250.8 to mut-16/siRNAs, they made a double mutant and examined body length as a proxy for developmental stage. Here, they observed a partial rescue of the mut-16 size defect by B0250.8 mutation. Finally, the authors also highlight data from further meta-analysis, which predicts the recognition of B0250.8 by several piRNAs. Also based on existing data from the literature, the authors link loss of Piwi (PRG-1), which binds piRNAs, to a depletion of 22G-RNAs targeting B0250.8 and an upregulation of B0250.8 expression in gonads, suggesting that piRNAs are the primary small RNAs that target B0250.8 for downregulation. The data in this portion of the manuscript are intriguing, but somewhat preliminary and incomplete, as they are based on little primary experimentation and a collection of different datasets (which have been acquired by slightly different methods in most cases). This portion of the study would require subsequent experimentation to firmly establish this mechanistic link. For example, to be able to claim that "the N2 toxin allele has acquired mutations that enable piRNA binding to initiate MUT-16-dependent 22G small RNA amplification that targets the transcript for degradation" the identified piRNA sites should be mutated and protein and transcript levels analysed in wild-type and in the strain with mutated piRNA sites. At a minimum, the protein levels in wild-type and mut-16, prg-1, and/or wago-1 mutants should be measured by western blot and/or by live imaging (introducing a GFP or some other tag to the endogenous protein via CRISPR editing) to show that the toxin is not accumulated as a protein in wt, but increases in levels in these mutants. mRNA levels in Figure S5A suggest there is still some expression of the B0250.8 transcript in a wild-type situation.
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NATIONAL DISASTER RISKFINANCING FRAMEWORKAND IMPLEMENTATION PLAN
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we used a very high level um uh commu communication that this build an I here and like any good intelligence it has a multiscale hierarchical control where it took care of all of the downstream molecular um details.
for - example - importance of multiscale hierarchical intelligence and control - Michael Levin - high level instruction is issued and the multiscale structure ensures that all the lower level details are executed - like a software function call
new plexmark - person assigned to each comment in multiplayer conversational environment - have a way to - detect then - discriminate and finally - tag - each sequentially different conversant' s comments in the conversation - This will help with Indyweb provenance by attributing the person with each sentence
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Random idea: it could be neat if we added tooltips to the sample code so that the user sees an explanation of a tag when they move the mouse over it.
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Author response:
Public Reviews:
Reviewer #1 (Public Review):
Summary:
In their manuscript entitled 'The domesticated transposon protein L1TD1 associates with its ancestor L1 ORF1p to promote LINE-1 retrotransposition', Kavaklıoğlu and colleagues delve into the role of L1TD1, an RNA binding protein (RBP) derived from a LINE1 transposon. L1TD1 proves crucial for maintaining pluripotency in embryonic stem cells and is linked to cancer progression in germ cell tumors, yet its precise molecular function remains elusive. Here, the authors uncover an intriguing interaction between L1TD1 and its ancestral LINE-1 retrotransposon.
The authors delete the DNA methyltransferase DNMT1 in a haploid human cell line (HAP1), inducing widespread DNA hypo-methylation. This hypomethylation prompts abnormal expression of L1TD1. To scrutinize L1TD1's function in a DNMT1 knock-out setting, the authors create DNMT1/L1TD1 double knock-out cell lines (DKO). Curiously, while the loss of global DNA methylation doesn't impede proliferation, additional depletion of L1TD1 leads to DNA damage and apoptosis.
To unravel the molecular mechanism underpinning L1TD1's protective role in the absence of DNA methylation, the authors dissect L1TD1 complexes in terms of protein and RNA composition. They unveil an association with the LINE-1 transposon protein L1-ORF1 and LINE-1 transcripts, among others.
Surprisingly, the authors note fewer LINE-1 retro-transposition events in DKO cells than in DNMT1 KO alone.
Strengths:
The authors present compelling data suggesting the interplay of a transposon-derived human RNA binding protein with its ancestral transposable element. Their findings spur interesting questions for cancer types, where LINE1 and L1TD1 are aberrantly expressed.
Weaknesses:
Suggestions for refinement:
The initial experiment, inducing global hypo-methylation by eliminating DNMT1 in HAP1 cells, is intriguing and warrants a more detailed description. How many genes experience misregulation or aberrant expression? What phenotypic changes occur in these cells?
The transcriptome analysis of DNMT1 KO cells showed hundreds of deregulated genes upon DNMT1 ablation. As expected, the majority were up-regulated and gene ontology analysis revealed that among the strongest up-regulated genes were gene clusters with functions in “regulation of transcription from RNA polymerase II promoter” and “cell differentiation” and genes encoding proteins with KRAB domains. In addition, the de novo methyltransferases DNMT3A and DNMT3B were up-regulated in DNMT1 KO cells suggesting the set-up of compensatory mechanisms in these cells. We will include this data set in the revised version of the manuscript.
Why did the authors focus on L1TD1? Providing some of this data would be helpful to understand the rationale behind the thorough analysis of L1TD1.
We have previously discovered that conditional deletion of the maintenance DNA methyltransferase DNMT1 in the murine epidermis results not only in the up-regulation of mobile elements, such as IAPs but also the induced expression of L1TD1 ((Beck et al, 2021), Suppl. Table 1 and Author response image 1). Similary, L1TD1 expression was induced by treatment of primary human keratinocytes or squamous cell carcinoma cells with the DNMT inhibitor aza-deoxycytidine (Author response image 2 and 3). These finding are in accordance with the observation that inhibition of DNA methyltransferase activity by azadeoxycytidine in human non-small cell lung cancer cells (NSCLCs) results in upregulation of L1TD1 (Altenberger et al, 2017). Our interest in L1TD1 was further fueled by reports on a potential function of L1TD1 as prognostic tumor marker. We will include this information in the revised manuscript.
Author response image 1.
RT-qPCR of L1TD1 expression in cultured murine control and Dnmt1 Δ/Δker keratinocytes. mRNA levels of L1td1 were analyzed in keratinocytes isolated at P5 from conditional Dnmt1 knockout mice (Beck et al., 2021). Hprt expression was used for normalization of mRNA levels and wildtype control was set to 1. Data represent means ±s.d. with n=4. **P < 0.01 (paired t-test).
Author response image 2.
RT-qPCR analysis of L1TD1 expression in primary human keratinocytes. Cells were treated with 5-aza-2-deoxycidine for 24 hours or 48 hours, with PBS for 48 hours or were left untreated. 18S rRNA expression was used for normalization of mRNA levels and PBS control was set to 1. Data represent means ±s.d. with n=3. **P < 0.01 (paired t-test).
Author response image 3.
Induced L1TD1 expression upon DNMT inhibition in squamous cell carcinoma cell lines SCC9 and SCCO12. Cells were treated with 5-aza-2-deoxycidine for 24 hours, 48 hours or 6 days. (A) Western blot analysis of L1TD1 protein levels using beta-actin as loading control. (B) Indirect immunofluorescence microscopy analysis of L1TD1 expression in SCC9 cells. Nuclear DNA was stained with DAPI. Scale bar: 10 µm. (C) RT-qPCR analysis of L1TD1 expression in primary human keratinocytes. Cells were treated with 5-aza-2deoxycidine for 24 hours or 48 hours, with PBS for 48 hours or were left untreated. 18S rRNA expression was used for normalization of mRNA levels and PBS control was set to 1. Data represent means ±s.d. with n=3. P < 0.05, *P < 0.01 (paired t-test).
The finding that L1TD1/DNMT1 DKO cells exhibit increased apoptosis and DNA damage but decreased L1 retro-transposition is unexpected. Considering the DNA damage associated with retro-transposition and the DNA damage and apoptosis observed in L1TD1/DNMT1 DKO cells, one would anticipate the opposite outcome. Could it be that the observation of fewer transposition-positive colonies stems from the demise of the most transposition-positive colonies? Further exploration of this phenomenon would be intriguing.
This is an important point and we were aware of this potential problem. Therefore, we calibrated the retrotransposition assay by transfection with a blasticidin resistance gene vector to take into account potential differences in cell viability and blasticidin sensitivity. Thus, the observed reduction in L1 retrotransposition efficiency is not an indirect effect of reduced cell viability.
Based on previous studies with hESCs, it is likely that, in addition to its role in retrotransposition, L1TD1 has additional functions in the regulation of cell proliferation and differentiation. L1TD1 might therefore attenuate the effect of DNMT1 loss in KO cells generating an intermediate phenotype (as pointed out by Reviewer 2) and simultaneous loss of both L1TD1 and DNMT1 results in more pronounced effects on cell viability.
Reviewer #2 (Public Review):
In this study, Kavaklıoğlu et al. investigated and presented evidence for the role of domesticated transposon protein L1TD1 in enabling its ancestral relative, L1 ORF1p, to retrotranspose in HAP1 human tumor cells. The authors provided insight into the molecular function of L1TD1 and shed some clarifying light on previous studies that showed somewhat contradictory outcomes surrounding L1TD1 expression. Here, L1TD1 expression was correlated with L1 activation in a hypomethylation-dependent manner, due to DNMT1 deletion in the HAP1 cell line. The authors then identified L1TD1-associated RNAs using RIP-Seq, which displays a disconnect between transcript and protein abundance (via Tandem Mass Tag multiplex mass spectrometry analysis). The one exception was for L1TD1 itself, which is consistent with a model in which the RNA transcripts associated with L1TD1 are not directly regulated at the translation level. Instead, the authors found the L1TD1 protein associated with L1-RNPs, and this interaction is associated with increased L1 retrotransposition, at least in the contexts of HAP1 cells. Overall, these results support a model in which L1TD1 is restrained by DNA methylation, but in the absence of this repressive mark, L1TD1 is expressed and collaborates with L1 ORF1p (either directly or through interaction with L1 RNA, which remains unclear based on current results), leads to enhances L1 retrotransposition. These results establish the feasibility of this relationship existing in vivo in either development, disease, or both.
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www.biorxiv.org www.biorxiv.org
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Author response:
The following is the authors’ response to the original reviews.
Public Reviews:
Reviewer #1 (Public Review):
Summary:
In their manuscript entitled 'The domesticated transposon protein L1TD1 associates with its ancestor L1 ORF1p to promote LINE-1 retrotransposition', Kavaklıoğlu and colleagues delve into the role of L1TD1, an RNA binding protein (RBP) derived from a LINE1 transposon. L1TD1 proves crucial for maintaining pluripotency in embryonic stem cells and is linked to cancer progression in germ cell tumors, yet its precise molecular function remains elusive. Here, the authors uncover an intriguing interaction between L1TD1 and its ancestral LINE-1 retrotransposon.
The authors delete the DNA methyltransferase DNMT1 in a haploid human cell line (HAP1), inducing widespread DNA hypo-methylation. This hypomethylation prompts abnormal expression of L1TD1. To scrutinize L1TD1's function in a DNMT1 knock-out setting, the authors create DNMT1/L1TD1 double knock-out cell lines (DKO). Curiously, while the loss of global DNA methylation doesn't impede proliferation, additional depletion of L1TD1 leads to DNA damage and apoptosis.
To unravel the molecular mechanism underpinning L1TD1's protective role in the absence of DNA methylation, the authors dissect L1TD1 complexes in terms of protein and RNA composition. They unveil an association with the LINE-1 transposon protein L1-ORF1 and LINE-1 transcripts, among others.
Surprisingly, the authors note fewer LINE-1 retro-transposition events in DKO cells than in DNMT1 KO alone.
Strengths:
The authors present compelling data suggesting the interplay of a transposon-derived human RNA binding protein with its ancestral transposable element. Their findings spur interesting questions for cancer types, where LINE1 and L1TD1 are aberrantly expressed.
Weaknesses:
Suggestions for refinement:
The initial experiment, inducing global hypo-methylation by eliminating DNMT1 in HAP1 cells, is intriguing and warrants a more detailed description. How many genes experience misregulation or aberrant expression? What phenotypic changes occur in these cells?
This is an excellent suggestion. We have gene expression data on WT versus DNMT1 KO HAP1 cells and have included them now as Suppl. Figure S1. The transcriptome analysis of DNMT1 KO cells showed hundreds of deregulated genes upon DNMT1 ablation. As expected, the majority were up-regulated and gene ontology analysis revealed that among the strongest up-regulated genes were gene clusters with functions in “regulation of transcription from RNA polymerase II promoter” and “cell differentiation” and genes encoding proteins with KRAB domains. In addition, the de novo methyltransferases DNMT3A and DNMT3B were up-regulated in DNMT1 KO cells suggesting the set-up of compensatory mechanisms in these cells.
Why did the authors focus on L1TD1? Providing some of this data would be helpful to understand the rationale behind the thorough analysis of L1TD1.
We have previously discovered that conditional deletion of the maintenance DNA methyltransferase DNMT1 in the murine epidermis results not only in the up-regulation of mobile elements, such as IAPs but also the induced expression of L1TD1 ([1], Suppl. Table 1 and Author response image 1). Similary, L1TD1 expression was induced by treatment of primary human keratinocytes or squamous cell carcinoma cells with the DNMT inhibitor azadeoxycytidine (Author response images 2 and 3). These findings are in accordance with the observation that inhibition of DNA methyltransferase activity by aza-deoxycytidine in human non-small cell lung cancer cells (NSCLCs) results in up-regulation of L1TD1 [2]. Our interest in L1TD1 was further fueled by reports on a potential function of L1TD1 as prognostic tumor marker. We have included this information in the last paragraph of the Introduction in the revised manuscript.
Author response image 1. RT-qPCR of L1TD1 expression in cultured murine control and Dnmt1 Δ/Δker keratinocytes. mRNA levels of L1td1 were analyzed in keratinocytes isolated at P5 from conditional Dnmt1 knockout mice [1]. Hprt expression was used for normalization of mRNA levels and wildtype control was set to 1. Data represent means ±s.d. with n=4. **P < 0.01 (paired t-test).
Author response image 2. RT-qPCR analysis of L1TD1 expression in primary human keratinocytes. Cells were treated with 5-aza-2-deoxycidine for 24 hours or 48 hours, with PBS for 48 hours or were left untreated. 18S rRNA expression was used for normalization of mRNA levels and PBS control was set to 1. Data represent means ±s.d. with n=3. **P < 0.01 (paired t-test).
Author response image 3. Induced L1TD1 expression upon DNMT inhibition in squamous cell carcinoma cell lines SCC9 and SCCO12. Cells were treated with 5-aza-2-deoxycidine for 24 hours, 48 hours or 6 days. (A) Western blot analysis of L1TD1 protein levels using beta-actin as loading control. (B) Indirect immunofluorescence microscopy analysis of L1TD1 expression in SCC9 cells. Nuclear DNA was stained with DAPI. Scale bar: 10 µm. (C) RT-qPCR analysis of L1TD1 expression in primary human keratinocytes. Cells were treated with 5-aza-2deoxycidine for 24 hours or 48 hours, with PBS for 48 hours or were left untreated. 18S rRNA expression was used for normalization of mRNA levels and PBS control was set to 1. Data represent means ±s.d. with n=3. *P < 0.05, **P < 0.01 (paired t-test).
The finding that L1TD1/DNMT1 DKO cells exhibit increased apoptosis and DNA damage but decreased L1 retro-transposition is unexpected. Considering the DNA damage associated with retro-transposition and the DNA damage and apoptosis observed in L1TD1/DNMT1 DKO cells, one would anticipate the opposite outcome. Could it be that the observation of fewer transposition-positive colonies stems from the demise of the most transposition-positive colonies? Further exploration of this phenomenon would be intriguing.
This is an important point and we were aware of this potential problem. Therefore, we calibrated the retrotransposition assay by transfection with a blasticidin resistance gene vector to take into account potential differences in cell viability and blasticidin sensitivity. Thus, the observed reduction in L1 retrotransposition efficiency is not an indirect effect of reduced cell viability. We have added a corresponding clarification in the Results section on page 8, last paragraph.
Based on previous studies with hESCs and germ cell tumors [3], it is likely that, in addition to its role in retrotransposition, L1TD1 has further functions in the regulation of cell proliferation and differentiation. L1TD1 might therefore attenuate the effect of DNMT1 loss in KO cells generating an intermediate phenotype (as pointed out by Reviewer 2) and simultaneous loss of both L1TD1 and DNMT1 results in more pronounced effects on cell viability. This is in agreement with the observation that a subset of L1TD1 associated transcripts encode proteins involved in the control of cell division and cell cycle. It is possible that subtle changes in the expression of these protein that were not detected in our mass spectrometry approach contribute to the antiproliferative effect of L1TD1 depletion as discussed in the Discussion section of the revised manuscript.
Reviewer #2 (Public Review):
In this study, Kavaklıoğlu et al. investigated and presented evidence for the role of domesticated transposon protein L1TD1 in enabling its ancestral relative, L1 ORF1p, to retrotranspose in HAP1 human tumor cells. The authors provided insight into the molecular function of L1TD1 and shed some clarifying light on previous studies that showed somewhat contradictory outcomes surrounding L1TD1 expression. Here, L1TD1 expression was correlated with L1 activation in a hypomethylation-dependent manner, due to DNMT1 deletion in the HAP1 cell line. The authors then identified L1TD1-associated RNAs using RIP-Seq, which displays a disconnect between transcript and protein abundance (via Tandem Mass Tag multiplex mass spectrometry analysis). The one exception was for L1TD1 itself, which is consistent with a model in which the RNA transcripts associated with L1TD1 are not directly regulated at the translation level. Instead, the authors found the L1TD1 protein associated with L1-RNPs, and this interaction is associated with increased L1 retrotransposition, at least in the contexts of HAP1 cells. Overall, these results support a model in which L1TD1 is restrained by DNA methylation, but in the absence of this repressive mark, L1TD1 is expressed and collaborates with L1 ORF1p (either directly or through interaction with L1 RNA, which remains unclear based on current results), leads to enhances L1 retrotransposition. These results establish the feasibility of this relationship existing in vivo in either development, disease, or both.
Recommendations for the authors:
Reviewer #2 (Recommendations For The Authors):
Major
(1) The study only used one knockout (KO) cell line generated by CRISPR/Cas9. Considering the possibility of an off-target effect, I suggest the authors attempt one or both of these suggestions.
A) Generate or acquire a similar DMNT1 deletion that uses distinct sgRNAs, so that the likelihood of off-targets is negligible. A few simple experiments such as qRT-PCR would be sufficient to suggest the same phenotype.
B) Confirm the DNMT1 depletion also by siRNA/ASO KD to phenocopy the KO effect. (2) In addition to the strategies to demonstrate reproducibility, a rescue experiment restoring DNMT1 to the KO or KD cells would be more convincing. (Partial rescue would suffice in this case, as exact endogenous expression levels may be hard to replicate).
We have undertook several approaches to study the effect of DNMT1 loss or inactivation: As described above, we have generated a conditional KO mouse with ablation of DNMT1 in the epidermis. DNMT1-deficient keratinocytes isolated from these mice show a significant increase in L1TD1 expression. In addition, treatment of primary human keratinocytes and two squamous cell carcinoma cell lines with the DNMT inhibitor aza-deoxycytidine led to upregulation of L1TD1 expression. Thus, the derepression of L1TD1 upon loss of DNMT1 expression or activity is not a clonal effect. Also, the spectrum of RNAs identified in RIP experiments as L1TD1-associated transcripts in HAP1 DNMT1 KO cells showed a strong overlap with the RNAs isolated by a related yet different method in human embryonic stem cells. When it comes to the effect of L1TD1 on L1-1 retrotranspostion, a recent study has reported a similar effect of L1TD1 upon overexpression in HeLa cells [4].
All of these points together help to convince us that our findings with HAP1 DNMT KO are in agreement with results obtained in various other cell systems and are therefore not due to off-target effects. With that in mind, we would pursue the suggestion of Reviewer 1 to analyze the effects of DNA hypomethylation upon DNMT1 ablation.
(3) As stated in the introduction, L1TD1 and ORF1p share "sequence resemblance" (Martin 2006). Is the L1TD1 antibody specific or do we see L1 ORF1p if Fig 1C were uncropped? (6) Is it possible the L1TD1 antibody binds L1 ORF1p? This could make Figure 2D somewhat difficult to interpret. Some validation of the specificity of the L1TD1 antibody would remove this concern (see minor concern below).
This is a relevant question. We are convinced that the L1TD1 antibody does not crossreact with L1 ORF1p for the following reasons: Firstly, the antibody does not recognize L1 ORF1p (40 kDa) in the uncropped Western blot for Figure 1C (Author response image 4A). Secondly, the L1TD1 antibody gives only background signals in DKO cells in the indirect immunofluorescence experiment shown in Figure 1E of the manuscript.
Thirdly, the immunogene sequence of L1TD1 that determines the specificity of the antibody was checked in the antibody data sheet from Sigma Aldrich. The corresponding epitope is not present in the L1 ORF1p sequence. Finally, we have shown that the ORF1p antibody does not cross-react with L1TD1 (Author response image 4B).
Author response image 4. (A) Uncropped L1TD1 Western blot shown in Figure 1C. An unspecific band is indicated by an asterisk. (B) Westernblot analysis of WT, KO and DKO cells with L1 ORF1p antibody.
(4) In abstract (P2), the authors mentioned that L1TD1 works as an RNA chaperone, but in the result section (P13), they showed that L1TD1 associates with L1 ORF1p in an RNAindependent manner. Those conclusions appear contradictory. Clarification or revision is required.
Our findings that both proteins bind L1 RNA, and that L1TD1 interacts with ORF1p are compatible with a scenario where L1TD1/ORF1p heteromultimers bind to L1 RNA. The additional presence of L1TD1 might thereby enhance the RNA chaperone function of ORF1p. This model is visualized now in Suppl. Figure S7C.
(5) Figure 2C fold enrichment for L1TD1 and ARMC1 is a bit difficult to fully appreciate. A 100 to 200-fold enrichment does not seem physiological. This appears to be a "divide by zero" type of result, as the CT for these genes was likely near 40 or undetectable. Another qRT-PCRbased approach (absolute quantification) would be a more revealing experiment.
This is the validation of the RIP experiments and the presentation mode is specifically developed for quantification of RIP assays (Sigma Aldrich RIP-qRT-PCR: Data Analysis Calculation Shell). The unspecific binding of the transcript in the absence of L1TD1 in DNMT1/L1TD1 DKO cells is set to 1 and the value in KO cells represents the specific binding relative the unspecific binding. The calculation also corrects for potential differences in the abundance of the respective transcript in the two cell lines. This is not a physiological value but the quantification of specific binding of transcripts to L1TD1. GAPDH as negative control shows no enrichment, whereas specifically associated transcripts show strong enrichement. We have explained the details of RIPqRT-PCR evaluation in Materials and Methods (page 14) and the legend of Figure 2C in the revised manuscript.
(6) Is it possible the L1TD1 antibody binds L1 ORF1p? This could make Figure 2D somewhat difficult to interpret. Some validation of the specificity of the L1TD1 antibody would remove this concern (see minor concern below).
See response to (3).
(7) Figure S4A and S4B: There appear to be a few unusual aspects of these figures that should be pointed out and addressed. First, there doesn't seem to be any ORF1p in the Input (if there is, the exposure is too low). Second, there might be some L1TD1 in the DKO (lane 2) and lane 3. This could be non-specific, but the size is concerning. Overexposure would help see this.
The ORF1p IP gives rise to strong ORF1p signals in the immunoprecipitated complexes even after short exposure. Under these contions ORF1p is hardly detectable in the input. Regarding the faint band in DKO HAP1 cells, this might be due to a technical problem during Western blot loading. Therefore, the input samples were loaded again on a Western blot and analyzed for the presence of ORF1p, L1TD1 and beta-actin (as loading control) and shown as separate panel in Suppl. Figure S4A.
(8) Figure S4C: This is related to our previous concerns involving antibody cross-reactivity. Figure 3E partially addresses this, where it looks like the L1TD1 "speckles" outnumber the ORF1p puncta, but overlap with all of them. This might be consistent with the antibody crossreacting. The western blot (Figure 3C) suggests an upregulation of ORF1p by at least 2-3x in the DKO, but the IF image in 3E is hard to tell if this is the case (slightly more signal, but fewer foci). Can you return to the images and confirm the contrast are comparable? Can you massively overexpose the red channel in 3E to see if there is residual overlap?
In Figure 3E the L1TD1 antibody gives no signal in DNMT1/L1TD1 DKO cells confirming that it does not recognize ORF1p. In agreement with the Western blot in Figure 3C the L1 ORF1p signal in Figure 3E is stronger in DKO cells. In DNMT1 KO cells the L1 ORF1p antibody does not recognize all L1TD1 speckles. This result is in agreement with the Western blot shown above in Figure R4B and indicates that the L1 ORF1p antibody does not recognize the L1TD1 protein. The contrast is comparable and after overexposure there are still L1TD1 specific speckles. This might be due to differences in abundance of the two proteins.
(9) The choice of ARMC1 and YY2 is unclear. What are the criteria for the selection?
ARMC1 was one of the top hits in a pilot RIP-seq experiment (IP versus input and IP versus IgG IP). In the actual RIP-seq experiment with DKO HAP1 cells instead of IgG IP as a negative control, we found ARMC1 as an enriched hit, although it was not among the top 5 hits. The results from the 2nd RIP-seq further confirmed the validity of ARMC1 as an L1TD1-interacting transcript. YY2 was of potential biological relevance as an L1TD1 target due to the fact that it is a processed pseudogene originating from YY1 mRNA as a result of retrotransposition. This is mentioned on page 6 of the revised manuscript.
(10) (P16) L1 is the only protein-coding transposon that is active in humans. This is perhaps too generalized of a statement as written. Other examples are readily found in the literature. Please clarify.
We will tone down this statement in the revised manuscript.
(11) In both the abstract and last sentence in the discussion section (P17), embryogenesis is mentioned, but this is not addressed at all in the manuscript. Please refrain from implying normal biological functions based on the results of this study unless appropriate samples are used to support them.
Much of the published data on L1TD1 function are related to embryonic stem cells [3-7]. Therefore, it is important to discuss our findings in the context of previous reports.
(12) Figure 3E: The format of Figures 1A and 3E are internally inconsistent. Please present similar data/images in a cohesive way throughout the manuscript.
We show now consistent IF Figures in the revised manuscript.
Minor:
(1) Intro:
- Is L1Td1 in mice and Humans? How "conserved" is it and does this suggest function?
Murine and human L1TD1 proteins share 44% identity on the amino acid level and it was suggested that the corresponding genes were under positive selection during evolution with functions in transposon control and maintenance of pluripotency [8].
- Why HAP1? (Haploid?) The importance of this cell line is not clear.
HAP1 is a nearly haploid human cancer cell line derived from the KBM-7 chronic myelogenous leukemia (CML) cell line [9, 10]. Due to its haploidy is perfectly suited and widely used for loss-of-function screens and gene editing. After gene editing cells can be used in the nearly haploid or in the diploid state. We usually perform all experiments with diploid HAP1 cell lines. Importantly, in contrast to other human tumor cell lines, this cell line tolerates ablation of DNMT1. We have included a corresponding explanation in the revised manuscript on page 5, first paragraph.
- Global methylation status in DNMT1 KO? (Methylations near L1 insertions, for example?)
The HAP1 DNMT1 KO cell line with a 20 bp deletion in exon 4 used in our study was validated in the study by Smits et al. [11]. The authors report a significant reduction in overall DNA methylation. However, we are not aware of a DNA methylome study on this cell line. We show now data on the methylation of L1 elements in HAP1 cells and upon DNMT1 deletion in the revised manuscript in Suppl. Figure S1B.
(2) Figure 1:
- Figure 1C. Why is LMNB used instead of Actin (Fig1D)?
We show now beta-actin as loading control in the revised manuscript.
- Figure 1G shows increased Caspase 3 in KO, while the matching sentence in the result section skips over this. It might be more accurate to mention this and suggest that the single KO has perhaps an intermediate phenotype (Figure 1F shows a slight but not significant trend).
We fully agree with the reviewer and have changed the sentence on page 6, 2nd paragraph accordingly.
- Would 96 hrs trend closer to significance? An interpretation is that L1TD1 loss could speed up this negative consequence.
We thank the reviewer for the suggestion. We have performed a time course experiment with 6 biological replicas for each time point up to 96 hours and found significant changes in the viability upon loss of DNMT1 and again significant reduction in viability upon additional loss of L1TD1 (shown in Figure 1F). These data suggest that as expexted loss of DNMT1 leads to significant reduction viability and that additional ablation of L1TD1 further enhances this effect.
- What are the "stringent conditions" used to remove non-specific binders and artifacts (negative control subtraction?)
Yes, we considered only hits from both analyses, L1TD1 IP in KO versus input and L1TD1 IP in KO versus L1TD1 IP in DKO. This is now explained in more detail in the revised manuscript on page 6, 3rd paragraph.
(3) Figure 2:
- Figure 2A is a bit too small to read when printed.
We have changed this in the revised manuscript.
- Since WT and DKO lack detectable L1TD1, would you expect any difference in RIP-Seq results between these two?
Due to the lack of DNMT1 and the resulting DNA hypomethylation, DKO cells are more similar to KO cells than WT cells with respect to the expressed transcripts.
- Legend says selected dots are in green (it appears blue to me).
We have changed this in the revised manuscript.
- Would you recover L1 ORF1p and its binding partners in the KO? (Is the antibody specific in the absence of L1TD1 or can it recognize L1?) I noticed an increase in ORF1p in the KO in Figure 3C.
Thank you for the suggestion. Yes, L1 ORF1p shows slightly increased expression in the proteome analysis and we have marked the corresponding dot in the Volcano plot (Figure 3A).
- Should the figure panel reference near the (Rosspopoff & Trono) reference instead be Sup S1C as well? Otherwise, I don't think S1C is mentioned at all.
- What are the red vs. green dots in 2D? Can you highlight ERV and ALU with different colors?
We added the reference to Suppl. Figure S1C (now S3C) in the revised manuscript. In Figure 2D L1 elements are highlighted in green, ERV elements in yellow, and other associated transposon transcripts in red.
- Which L1 subfamily from Figure 2D is represented in the qRT-PCR in 2E "LINE-1"? Do the primers match a specific L1 subfamily? If so, which?
We used primers specific for the human L1.2 subfamily.
- Pulling down SINE element transcripts makes some sense, as many insertions "borrow" L1 sequences for non-autonomous retro transposition, but can you speculate as to why ERVs are recovered? There should be essentially no overlap in sequence.
In the L1TD1 evolution paper [8], a potential link between L1TD1 and ERV elements was discussed:
"Alternatively, L1TD1 in sigmodonts could play a role in genome defense against another element active in these genomes. Indeed, the sigmodontine rodents have a highly active family of ERVs, the mysTR elements [46]. Expansion of this family preceded the death of L1s, but these elements are very active, with 3500 to 7000 species-specific insertions in the L1-extinct species examined [47]. This recent ERV amplification in Sigmodontinae contrasts with the megabats (where L1TD1 has been lost in many species); there are apparently no highly active DNA or RNA elements in megabats [48]. If L1TD1 can suppress retroelements other than L1s, this could explain why the gene is retained in sigmodontine rodents but not in megabats."
Furthermore, Jin et al. report the binding of L1TD1 to repetitive sequences in transcripts [12]. It is possible that some of these sequences are also present in ERV RNAs.
- Is S2B a screenshot? (the red underline).
No, it is a Powerpoint figure, and we have removed the red underline.
(4) Figure 3:
- Text refers to Figure 3B as a western blot. Figure 3B shows a volcano plot. This is likely 3C but would still be out of order (3A>3C>3B referencing). I think this error is repeated in the last result section.
- Figure and legends fail to mention what gene was used for ddCT method (actin, gapdh, etc.).
- In general, the supplemental legends feel underwritten and could benefit from additional explanations. (Main figures are appropriate but please double-check that all statistical tests have been mentioned correctly).
Thank you for pointing this out. We have corrected these errors in the revised manuscript.
(5) Discussion:
-Aluy connection is interesting. Is there an "Alu retrotransposition reporter assay" to test whether L1TD1 enhances this as well?
Thank you for the suggestion. There is indeed an Alu retrotransposition reporter assay reported be Dewannieux et al. [13]. The assay is based on a Neo selection marker. We have previously tested a Neo selection-based L1 retrotransposition reporter assay, but this system failed to properly work in HAP1 cells, therefore we switched to a blasticidinbased L1 retrotransposition reporter assay. A corresponding blasticidin-based Alu retrotransposition reporter assay might be interesting for future studies (mentioned in the Discussion, page 11 paragraph 4 of the revised manuscript.
(6) Material and Methods :
- The number of typos in the materials and methods is too numerous to list. Instead, please refer to the next section that broadly describes the issues seen throughout the manuscript.
Writing style
(1) Keep a consistent style throughout the manuscript: for example, L1 or LINE-1 (also L1 ORF1p or LINE-1 ORF1p); per or "/"; knockout or knock-out; min or minute; 3 times or three times; media or medium. Additionally, as TE naming conventions are not uniform, it is important to maintain internal consistency so as to not accidentally establish an imprecise version.
(2) There's a period between "et al" and the comma, and "et al." should be italic.
(3) The authors should explain what the key jargon is when it is first used in the manuscript, such as "retrotransposon" and "retrotransposition".
(4) The authors should show the full spelling of some acronyms when they use it for the first time, such as RNA Immunoprecipitation (RIP).
(5) Use a space between numbers and alphabets, such as 5 µg.
(6) 2.0 × 105 cells, that's not an "x".
(7) Numbers in the reference section are lacking (hard to parse).
(8) In general, there are a significant number of typos in this draft which at times becomes distracting. For example, (P3) Introduction: Yet, co-option of TEs thorough (not thorough, it should be through) evolution has created so-called domesticated genes beneficial to the gene network in a wide range of organisms. Please carefully revise the entire manuscript for these minor issues that collectively erode the quality of this submission.
Thank you for pointing out these mistakes. We have corrected them in the revised manuscript. A native speaker from our research group has carefully checked the paper. In summary, we have added Supplementary Figure S7C and have changed Figures 1C, 1E, 1F, 2A, 2D, 3A, 4B, S3A-D, S4B and S6A based on these comments.
REFERENCES
(1) Beck, M.A., et al., DNA hypomethylation leads to cGAS-induced autoinflammation in the epidermis. EMBO J, 2021. 40(22): p. e108234.
(2) Altenberger, C., et al., SPAG6 and L1TD1 are transcriptionally regulated by DNA methylation in non-small cell lung cancers. Mol Cancer, 2017. 16(1): p. 1.
(3) Narva, E., et al., RNA-binding protein L1TD1 interacts with LIN28 via RNA and is required for human embryonic stem cell self-renewal and cancer cell proliferation. Stem Cells, 2012. 30(3): p. 452-60.
(4) Jin, S.W., et al., Dissolution of ribonucleoprotein condensates by the embryonic stem cell protein L1TD1. Nucleic Acids Res, 2024. 52(6): p. 3310-3326.
(5) Emani, M.R., et al., The L1TD1 protein interactome reveals the importance of posttranscriptional regulation in human pluripotency. Stem Cell Reports, 2015. 4(3): p. 519-28.
(6) Santos, M.C., et al., Embryonic Stem Cell-Related Protein L1TD1 Is Required for Cell Viability, Neurosphere Formation, and Chemoresistance in Medulloblastoma. Stem Cells Dev, 2015. 24(22): p. 2700-8.
(7) Wong, R.C., et al., L1TD1 is a marker for undifferentiated human embryonic stem cells. PLoS One, 2011. 6(4): p. e19355.
(8) McLaughlin, R.N., Jr., et al., Positive selection and multiple losses of the LINE-1-derived L1TD1 gene in mammals suggest a dual role in genome defense and pluripotency. PLoS Genet, 2014. 10(9): p. e1004531.
(9) Andersson, B.S., et al., Ph-positive chronic myeloid leukemia with near-haploid conversion in vivo and establishment of a continuously growing cell line with similar cytogenetic pattern. Cancer Genet Cytogenet, 1987. 24(2): p. 335-43.
(10) Carette, J.E., et al., Ebola virus entry requires the cholesterol transporter Niemann-Pick C1. Nature, 2011. 477(7364): p. 340-3.
(11) Smits, A.H., et al., Biological plasticity rescues target activity in CRISPR knock outs. Nat Methods, 2019. 16(11): p. 1087-1093.
(12) Jin, S.W., et al., Dissolution of ribonucleoprotein condensates by the embryonic stem cell protein L1TD1. Nucleic Acids Res, 2024.
(13) Dewannieux, M., C. Esnault, and T. Heidmann, LINE-mediated retrotransposition of marked Alu sequences. Nat Genet, 2003. 35(1): p. 41-8.
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Author Response:
The following is the authors' response to the original reviews.
Reply to Public Reviews:
Reply to Reviewer #1:
This is a carefully performed and well-documented study to indicate that the FUS protein interacts with the GGGGCC repeat sequence in Drosophila fly models, and the mechanism appears to include modulating the repeat structure and mitigating RAN translation. They suggest FUS, as well as a number of other G-quadruplex binding RNA proteins, are RNA chaperones, meaning they can alter the structure of the expanded repeat sequence to modulate its biological activities.
Response: We would like to thank the reviewer for her/his time for evaluating our manuscript. We are very happy to see the reviewer for highly appreciating our manuscript.
1. Overall this is a nicely done study with nice quantitation. It remains somewhat unclear from the data and discussions in exactly what way the authors mean that FUS is an RNA chaperone: is FUS changing the structure of the repeat or does FUS binding prevent it from folding into alternative in vivo structure?
Response: We appreciate the reviewer’s constructive comments. Indeed, we showed that FUS changes the higher-order structures of GGGGCC [G4C2] repeat RNA in vitro, and that FUS suppresses G4C2 RNA foci formation in vivo. According to the established definition of RNA chaperone, RNA chaperones are proteins changing the structures of misfolded RNAs without ATP use, resulting in the maintenance of proper RNAs folding (Rajkowitsich et al., 2007). Thus, we consider that FUS is classified into RNA chaperone. To clarify these interpretations, we revised the manuscript as follows.
(1) On page 10, line 215-219, the sentence “These results were in good agreement with our previous study on SCA31 showing the suppressive effects of FUS and other RBPs on RNA foci formation of UGGAA repeat RNA as RNA chaperones …” was changed to “These results were in good agreement with … RNA foci formation of UGGAA repeat RNA through altering RNA structures and preventing aggregation of misfolded repeat RNA as RNA chaperones …”.
(2) On page 17, line 363-366, the sentence “FUS directly binds to G4C2 repeat RNA and modulates its G-quadruplex structure, as evident by CD and NMR analyses (Figure 5), suggesting its functional role as an RNA chaperone.” was changed to “FUS directly binds to G4C2 repeat RNA and modulates its G-quadruplex structure as evident by CD and NMR analyses (Figure 5, Figure 5—figure supplement 2), and suppresses RNA foci formation in vivo (Figures 3A and 3B), suggesting its functional role as an RNA chaperone.”
Reply to Reviewer #2:
Fuijino et al. provide interesting data describing the RNA-binding protein, FUS, for its ability to bind the RNA produced from the hexanucleotide repeat expansion of GGGGCC (G4C2). This binding correlates with reductions in the production of toxic dipeptides and reductions in toxic phenotypes seen in (G4C2)30+ expressing Drosophila. Both FUS and G4C2 repeats of >25 are associated with ALS/FTD spectrum disorders. Thus, these data are important for increasing our understanding of potential interactions between multiple disease genes. However, further validation of some aspects of the provided data is needed, especially the expression data.
Response: We would like to thank the reviewer for her/his time for evaluating our manuscript and also for her/his important comments that helped to strengthen our manuscript.
Some points to consider when reading the work:
1. The broadly expressed GMR-GAL4 driver leads to variable tissue loss in different genotypes, potentially confounding downstream analyses dependent on viable tissue/mRNA levels.
Response: We thank the reviewer for this constructive comment. In the RT-qPCR experiments (Figures 1E, 3C, 4G, 6D and Figure 1—figure supplement 1C), the amounts of G4C2 repeat transcripts were normalized to those of gal4 transcripts expressed in the same tissue, to avoid potential confounding derived from the difference in tissue viability between genotypes, as the reviewer pointed out. To clarify this process, we have made the following change to the revised manuscript.
(1) On page 30, line 548-550, the sentence “The amounts of G4C2 repeat transcripts were normalized to those of gal4 transcripts in the same sample” was changed to “The amounts of G4C2 repeat transcripts were normalized to those of gal4 transcripts expressed in the same tissue to avoid potential confounding derived from the difference in tissue viability between genotypes”.
2. The relationship between FUS and foci formation is unclear and should be interpreted carefully.
Response: We appreciate the reviewer’s important comment. We apologize for the lack of clarity. We showed the relationship between FUS and RNA foci formation in our C9-ALS/FTD fly, that is, FUS suppresses RNA foci formation (Figures 3A and 3B), and knockdown of endogenous caz, a Drosophila homologue of FUS, enhanced it conversely (Figures 4E and 4F). We consider that FUS suppresses RNA foci formation through altering RNA structures and preventing aggregation of misfolded G4C2 repeat RNA as an RNA chaperone. To clarify these interpretations, we revised the manuscript as follows.
(1) On page 10, line 215-219, the sentence “These results were in good agreement with our previous study on SCA31 showing the suppressive effects of FUS and other RBPs on RNA foci formation of UGGAA repeat RNA as RNA chaperones …” was changed to “These results were in good agreement with … RNA foci formation of UGGAA repeat RNA through altering RNA structures and preventing aggregation of misfolded repeat RNA as RNA chaperones …”.
(2) On page 17, line 363-366, the sentence “FUS directly binds to G4C2 repeat RNA and modulates its G-quadruplex structure, as evident by CD and NMR analyses (Figure 5), suggesting its functional role as an RNA chaperone.” was changed to “FUS directly binds to G4C2 repeat RNA and modulates its G-quadruplex structure as evident by CD and NMR analyses (Figure 5, Figure 5—figure supplement 2), and suppresses RNA foci formation in vivo (Figures 3A and 3B), suggesting its functional role as an RNA chaperone.”
Reply to Reviewer #3:
In this manuscript Fujino and colleagues used C9-ALS/FTD fly models to demonstrate that FUS modulates the structure of (G4C2) repeat RNA as an RNA chaperone, and regulates RAN translation, resulting in the suppression of neurodegeneration in C9-ALS/FTD. They also confirmed that FUS preferentially binds to and modulates the G-quadruplex structure of (G4C2) repeat RNA, followed by the suppression of RAN translation. The potential significance of these findings is high since C9ORF72 repeat expansion is the most common genetic cause of ALS/FTD, especially in Caucasian populations and the DPR proteins have been considered the major cause of the neurodegenerations.
Response: We would like to thank the reviewer for her/his time for evaluating our manuscript. We are grateful to the reviewer for the insightful comments, which were very helpful for us to improve the manuscript.
1. While the effect of RBP as an RNA chaperone on (G4C2) repeat expansion is supposed to be dose-dependent according to (G4C2)n RNA expression, the first experiment of the screening for RBPs in C9-ALS/FTD flies lacks this concept. It is uncertain if the RBPs of the groups "suppression (weak)" and "no effect" were less or no ability of RNA chaperone or if the expression of the RBP was not sufficient, and if the RBPs of the group "enhancement" exacerbated the toxicity derived from (G4C2)89 RNA or the expression of the RBP was excessive. The optimal dose of any RBPs that bind to (G4C2) repeats may be able to neutralize the toxicity without the reduction of (G4C2)n RNA.
Response: We appreciate the reviewer’s constructive comments. We employed the site-directed transgenesis for the establishment of RBP fly lines, to ensure the equivalent expression levels of the inserted transgenes. We also evaluated the toxic effects of overexpressed RBPs themselves by crossbreeding with control EGFP flies, showing in Figure 1A. To clarify them, we have made the following changes to the revised manuscript.
(1) On page 8, line 166-168, the sentence “The variation in the effects of these G4C2 repeat-binding RBPs on G4C2 repeat-induced toxicity may be due to their different binding affinities to G4C2 repeat RNA, and their different roles in RNA metabolism.” was changed to “The variation in the effects of these G4C2 repeat-binding RBPs on G4C2 repeat-induced toxicity may be due to their different binding affinities to G4C2 repeat RNA, and the different toxicity of overexpressed RBPs themselves.”.
(2) On page 29, line 519-522, the sentence “By employing site-specific transgenesis using the pUASTattB vector, each transgene was inserted into the same locus of the genome, and was expected to be expressed at the equivalent levels.” was added.
2. In relation to issue 1, the rescue effect of FUS on the fly expressing (G4C2)89 (FUS-4) in Figure 4-figure supplement 1 seems weaker than the other flies expressing both FUS and (G4C2)89 in Figure 1 and Figure 1-figure supplement 2. The expression level of both FUS protein and (G4C2)89 RNA in each line is important from the viewpoint of therapeutic strategy for C9-ALS/FTD.
Response: We appreciate the reviewer’s important comment. The FUS-4 transgene is expected to be expressed at the equivalent level to the FUS-3 transgene, since they are inserted into the same locus of the genome by the site-directed transgenesis. Thus, we suppose that the weaker suppressive effect of FUS-4 coexpression on G4C2 repeat-induced eye degeneration can be attributed to the C-terminal FLAG tag that is fused to FUS protein expressed in FUS-4 fly line. Since the caz fly expresses caz protein also fused to FLAG tag at the C-terminus, we used this FUS-4 fly line to directly compare the effect of caz on G4C2 repeat-induced toxicity to that of FUS.
3. While hallmarks of C9ORF72 are the presence of DPRs and the repeat-containing RNA foci, the loss of function of C9ORF72 is also considered to somehow contribute to neurodegeneration. It is unclear if FUS reduces not only the DPRs but also the protein expression of C9ORF72 itself.
Response: We thank the reviewer for this comment. We agree that not only DPRs, but also toxic repeat RNA and the loss-of-function of C9ORF72 jointly contribute to the pathomechanisms of C9-ALS/FTD. Since Drosophila has no homolog corresponding to the human C9orf72 gene, the effect of FUS on C9orf72 expression cannot be assessed. Our fly models are useful for evaluating gain-of-toxic pathomechanisms such as RNA foci formation and RAN translation, and the association between FUS and loss-of function of C9ORF72 is beyond the scope of this study.
4. In Figure 5E-F, it cannot be distinguished whether FUS binds to GGGGCC repeats or the 5' flanking region. The same experiment should be done by using FUS-RRMmut to elucidate whether FUS binding is the major mechanism for this translational control. Authors should show that FUS binding to long GGGGCC repeats is important for RAN translation.
Response: We would like to thank the reviewer for these insightful comments. Following the reviewer’s suggestion, we perform in vitro translation assay again using FUS-RRMmut, which loses the binding ability to G4C2 repeat RNA as evident by the filter binding assay (Figure 5A), instead of BSA. The results are shown in the figures of Western blot analysis below. The addition of FUS to the translation system suppressed the expression levels of GA-Myc efficiently, whereas that of FUS-RRMmut did not. FUS decreased the expression level of GA-Myc at as low as 10nM, and nearly eliminated RAN translation activity at 100nM. At 400nM, FUS-RRMmut weakly suppressed the GA-Myc expression levels probably because of the residual RNA-binding activity. These results suggest that FUS suppresses RAN translation in vitro through direct interactions with G4C2 repeat RNA.
Unfortunately, RAN translation from short G4C2 repeat RNA was not investigated in our translation system, although the previous study reported the low efficacy of RAN translation from short G4C2 repeat RNA (Green et al., 2017).
Author response image 1.
(A) Western blot analysis of the GA-Myc protein in the samples from in vitro translation. (B) Quantification of the GA-Myc protein levels.
We have made the following changes to the revised manuscript.
(1) Figure 5F was replaced to new Figures 5F and 5G.
(2) On page 14-15, line 326-330, the sentence “Notably, the addition of FUS to this system decreased the expression level of GA-Myc in a dose-dependent manner, whereas the addition of the control bovine serum albumin (BSA) did not (Figure 5F).” was changed to “Notably, upon the addition to this translation system, FUS suppressed RAN translation efficiently, whereas FUS-RRMmut did not. FUS decreased the expression levels of GA-Myc at as low as 10nM, and nearly eliminated RAN translation activity at 100nM. At 400nM, FUS-RRMmut weakly suppressed the GA-Myc expression levels probably because of the residual RNA-binding activity (Figure 5F and 5G).”.
(3) On page 15, line 330-332, the sentence “Taken together, these results indicate that FUS suppresses RAN translation from G4C2 repeat RNA in vitro as an RNA chaperone.” was changed to “Taken together, these results indicate that FUS suppresses RAN translation in vitro through direct interactions with G4C2 repeat RNA as an RNA chaperone.”.
(4) On page 37, line 720-723, the sentence “For preparation of the FUS protein, the human FUS (WT) gene flanked at the 5¢ end with an Nde_I recognition site and at the 3¢ end with a _Xho_I recognition site was amplified by PCR from pUAST-_FUS.” was changed to “For preparation of the FUS proteins, the human FUS (WT) and FUS-RRMmut genes flanked at the 5¢ end with an Nde_I recognition site and at the 3¢ end with a _Xho_I recognition site was amplified by PCR from pUAST-_FUS and pUAST- FUS-RRMmut, respectively.”.
(5) On page 41, line 816-819, the sentence “FUS or BSA at each concentration (10, 100, and 1,000 nM) was added for translation in the lysate.” was changed to “FUS or FUS-RRMmut at each concentration (10, 100, 200, 400, and 1,000 nM) was preincubated with mRNA for 10 min to facilitate the interaction between FUS protein and G4C2 repeat RNA, and added for translation in the lysate.”.
5. It is not possible to conclude, as the authors have, that G-quadruplex-targeting RBPs are generally important for RAN translation (Figure 6), without showing whether RBPs that do not affect (G4C2)89 RNA levels lead to decreased DPR protein level or RNA foci.
Response: We appreciate the reviewer’s critical comment. Following the suggestion by the reviewer, we evaluate the effect of these G-quadruplex-targeting RBPs on RAN translation. We additionally performed immunohistochemistry of the eye imaginal discs of fly larvae expressing (G4C2)89 and these G-quadruplex-targeting RBPs. As shown in the figures of immunohistochemistry below, we found that coexpression of EWSR1, DDX3X, DDX5, and DDX17 significantly decreased the number of poly(GA) aggregates. The results suggest that these G-quadruplex-targeting RBPs regulate RAN translation as well as FUS.
Author response image 2.
(A) Immunohistochemistry of poly(GA) in the eye imaginal discs of fly larvae expressing (G4C2)89 and the indicated G-quadruplex-targeting RBPs. (B) Quantification of the number of poly(GA) aggregates.
We have made the following changes to the revised manuscript.
(1) Figures 6E and 6F were added.
(2) On page 6-7, line 135-137, the sentence “In addition, other G-quadruplex-targeting RBPs also suppressed G4C2 repeat-induced toxicity in our C9-ALS/FTD flies.” was changed to “In addition, other G-quadruplex-targeting RBPs also suppressed RAN translation and G4C2 repeat-induced toxicity in our C9-ALS/FTD flies.”.
(3) On page 15, line 344-346, the sentence “As expected, these RBPs also decreased the number of poly(GA) aggregates in the eye imaginal discs (Figures 6E and 6F).” was added.
(4) On page 15, line 346-347, the sentence “Their effects on G4C2 repeat-induced toxicity and repeat RNA expression were consistent with those of FUS.” was changed to “Their effects on G4C2 repeat-induced toxicity, repeat RNA expression, and RAN translation were consistent with those of FUS.”
(5) On page 16, line 355-357, the sentence “Thus, some G-quadruplex-targeting RBPs regulate G4C2 repeat-induced toxicity by binding to and possibly by modulating the G-quadruplex structure of G4C2 repeat RNA.” was changed to “Thus, some G-quadruplex-targeting RBPs regulate RAN translation and G4C2 repeat-induced toxicity by binding to and possibly by modulating the G-quadruplex structure of G4C2 repeat RNA.”
(6) On page 19, line 417-421, the sentence “We further found that G-quadruplex-targeting RNA helicases, including DDX3X, DDX5, and DDX17, which are known to bind to G4C2 repeat RNA (Cooper-Knock et al., 2014; Haeusler et al., 2014; Mori et al., 2013a; Xu et al., 2013), also alleviate G4C2 repeat-induced toxicity without altering the expression levels of G4C2 repeat RNA in our Drosophila models.” was changed to “We further found that G-quadruplex-targeting RNA helicases, … ,also suppress RAN translation and G4C2 repeat-induced toxicity without altering the expression levels of G4C2 repeat RNA in our Drosophila models.”.
Reply to Recommendations For The Authors:
1) It is not clear from the start that the flies they generated with the repeat have an artificial vs human intronic sequence ahead of the repeat. It would be nice if they presented somewhere the entire sequence of the insert. The reason being that it seems they also tested flies with the human intronic sequence, and the effect may not be as strong (line 234). In any case, in the future, with a new understanding of RAN translation, it would be nice to compare different transgenes, and so as much transparency as possible would be helpful regarding sequences. Can they include these data?
Response: We thank the editors and reviewers for this comment. We apologize for the lack of clarity. We used artificially synthesized G4C2 repeat sequences when generating constructs for (G4C2)n transgenic flies, so these constructs do not contain human intronic sequence ahead of the G4C2 repeat in the C9orf72 gene, as explained in the Materials and Methods section. To clarify the difference between our C9-ALS/FTD fly models and LDS-(G4C2)44GR-GFP fly model (Goodman et al., 2019), we have made the following change to the revised manuscript.
(1) Schema of the LDS-(G4C2)44GR-GFP construct was presented in Figure 3—figure supplement 1.
Furthermore, to maintain transparency of the study, we have provided the entire sequence of the insert as the following source file.
(2) The artificial sequences inserted in the pUAST vector for generation of the (G4C2)n flies were presented in Figure 1—figure supplement 1—source data 1.
2) It is really nice how they quantitated everything and showed individual data points.
Response: We thank the editors and reviewers for appreciating our data analysis method. All individual data points and statistical analyses are summarized in source data files.
3) So when they call FUS an RNA chaperone, are they simply meaning it is changing the structure of the repeat, or could it just be interacting with the repeat to coat the repeat and prevent it from folding into whatever in vivo structures? Can they speculate on why some RNA chaperones lead to presumed decay of the repeat and others do not? Can they discuss these points in the discussion? Detailed mechanistic understanding of RNA chaperones that ultimately promote decay of the repeat might be of highly significant therapeutic benefit.
Response: We appreciate these critical comments. Indeed, we showed that FUS changes the higher-order structures of G4C2 repeat RNA in vitro, and that FUS suppresses G4C2 RNA foci formation. According to the established definition of RNA chaperone, RNA chaperones are proteins changing the structures of misfolded RNAs without ATP use, resulting in the maintenance of proper RNAs folding (Rajkowitsich et al., 2007). Thus, we consider that FUS is classified into RNA chaperone. To clarify these interpretations, we revised the manuscript as follows.
(1) On page 10, line 215-219, the sentence “These results were in good agreement with our previous study on SCA31 showing the suppressive effects of FUS and other RBPs on RNA foci formation of UGGAA repeat RNA as RNA chaperones …” was changed to “These results were in good agreement with … RNA foci formation of UGGAA repeat RNA through altering RNA structures and preventing aggregation of misfolded repeat RNA as RNA chaperones …”.
(2) On page 17, line 363-366, the sentence “FUS directly binds to G4C2 repeat RNA and modulates its G-quadruplex structure, as evident by CD and NMR analyses (Figure 5), suggesting its functional role as an RNA chaperone.” was changed to “FUS directly binds to G4C2 repeat RNA and modulates its G-quadruplex structure as evident by CD and NMR analyses (Figure 5, Figure 5—figure supplement 2), and suppresses RNA foci formation in vivo (Figures 3A and 3B), suggesting its functional role as an RNA chaperone.”
Besides these RNA chaperones, we observed the expression of IGF2BP1, hnRNPA2B1, DHX9, and DHX36 decreased G4C2 repeat RNA expression levels. In addition, we recently reported that hnRNPA3 reduces G4C2 repeat RNA expression levels, leading to the suppression of neurodegeneration in C9-ALS/FTD fly models (Taminato et al., 2023). We speculate these RBPs could be involved in RNA decay pathways as components of the P-body or interactors with the RNA deadenylation machinery (Tran et al., 2004; Katahira et al., 2008; Geissler et al., 2016; Hubstenberger et al., 2017), possibly contributing to the reduced expression levels of G4C2 repeat RNA. To clarify these interpretations, we revised the manuscript as follows.
(3) On page 18, line 392-398, the sentences “Similarly, we recently reported that hnRNPA3 reduces G4C2 repeat RNA expression levels, leading to the suppression of neurodegeneration in C9-ALS/FTD fly models (Taminato et al., 2023). Interestingly, these RBPs have been reported to be involved in RNA decay pathways as components of the P-body or interactors with the RNA deadenylation machinery (Tran et al., 2004; Katahira et al., 2008; Geissler et al., 2016; Hubstenberger et al., 2017), possibly contributing to the reduced expression levels of G4C2 repeat RNA.” was added.
4) What is the level of the G4C2 repeat when they knock down caz? Is it possible that knockdown impacts the expression level of the repeat? Can they show this (or did they and I miss it)?
Response: We thank the editors and reviewers for this comment. The expression levels of G4C2 repeat RNA in (G4C2)89 flies were not altered by the knockdown of caz, as shown in Figure 4G.
5) A puzzling point is that FUS is supposed to be nuclear, so where is FUS in the brain in their lines? They suggest it modulates RAN translation, and presumably, that is in the cytoplasm. Is FUS when overexpressed now in part in the cytoplasm? Is the repeat dragging it into the cytoplasm? Can they address this in the discussion? If FUS is never found in vivo in the cytoplasm, then it raises the point that the impact they find of FUS on RAN translation might not reflect an in vivo situation with normal levels of FUS.
Response: We appreciate these important comments. We agree with the editors and reviewers that FUS is mainly localized in the nucleus. However, FUS is known as a nucleocytoplasmic shuttling RBP that can transport RNA into the cytoplasm. Indeed, FUS is reported to facilitate transport of actin-stabilizing protein mRNAs to function in the cytoplasm (Fujii et al., 2005). Thus, we consider that FUS binds to G4C2 repeat RNA in the cytoplasm and suppresses RAN translation in this study.
6) When they are using 2 copies of the driver and repeat, are they also using 2 copies of FUS? These are quite high levels of transgenes.
Response: We thank the editors and reviewers for this comment. We used only 1 copy of FUS when using 2 copies of GMR-Gal4 driver. Full genotypes of the fly lines used in all experiments are described in Supplementary file 1.
7) In Figure5-S1, FUS colocalizing with (G4C2)RNA is not clear. High-magnification images are recommended.
Response: We appreciate this constructive comment on the figure. Following the suggestion, high-magnification images are added in Figure 5—figure supplement 1.
8) I also suggest that the last sentence of the Discussion be revised as follows: Thus, our findings contribute not only to the elucidation of C9-ALS/FTD, but also to the elucidation of the repeat-associated pathogenic mechanisms underlying a broader range of neurodegenerative and neuropsychiatric disorders than previously thought, and it will advance the development of potential therapies for these diseases.
Response: We appreciate this recommendation. We have made the following change based on the suggested sentence.
(1) On page 20-21, line 455-459, “Thus, our findings contribute not only towards the elucidation of repeat-associated pathogenic mechanisms underlying a wider range of neuropsychiatric diseases than previously thought, but also towards the development of potential therapies for these diseases.” was changed to “Thus, our findings contribute to the elucidation of the repeat-associated pathogenic mechanisms underlying not only C9-ALS/FTD, but also a broader range of neuromuscular and neuropsychiatric diseases than previously thought, and will advance the development of potential therapies for these diseases.”.
Authors’ comment on previous eLife assessment:
We thank the editors and reviewers for appreciating our study. We mainly evaluated the function of human FUS protein on RAN translation and G4C2 repeat-induced toxicity using Drosophila expressing human FUS in vivo, and the recombinant human FUS protein in vitro. To validate that FUS functions as an endogenous regulator of RAN translation, we additionally evaluated the function of Drosophila caz protein as well. We are afraid that the first sentence of the eLife assessment, that is, “This important study demonstrates that the Drosophila FUS protein, the human homolog of which is implicated in amyotrophic lateral sclerosis (ALS) and related conditions, …” is somewhat misleading. We would be happy if you modify this sentence like “This important study demonstrates that the human FUS protein, which is implicated in amyotrophic lateral sclerosis (ALS) and related conditions, …”.
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Author response:
The following is the authors’ response to the original reviews.
eLife Assessment
This valuable study investigates how the neural representation of individual finger movements changes during the early period of sequence learning. By combining a new method for extracting features from human magnetoencephalography data and decoding analyses, the authors provide incomplete evidence of an early, swift change in the brain regions correlated with sequence learning, including a set of previously unreported frontal cortical regions. The addition of more control analyses to rule out that head movement artefacts influence the findings, and to further explain the proposal of offline contextualization during short rest periods as the basis for improvement performance would strengthen the manuscript.
We appreciate the Editorial assessment on our paper’s strengths and novelty. We have implemented additional control analyses to show that neither task-related eye movements nor increasing overlap of finger movements during learning account for our findings, which are that contextualized neural representations in a network of bilateral frontoparietal brain regions actively contribute to skill learning. Importantly, we carried out additional analyses showing that contextualization develops predominantly during rest intervals.
Public Reviews:
Reviewer #1 (Public review):
Summary:
This study addresses the issue of rapid skill learning and whether individual sequence elements (here: finger presses) are differentially represented in human MEG data. The authors use a decoding approach to classify individual finger elements and accomplish an accuracy of around 94%. A relevant finding is that the neural representations of individual finger elements dynamically change over the course of learning. This would be highly relevant for any attempts to develop better brain machine interfaces - one now can decode individual elements within a sequence with high precision, but these representations are not static but develop over the course of learning.
Strengths:
The work follows a large body of work from the same group on the behavioural and neural foundations of sequence learning. The behavioural task is well established and neatly designed to allow for tracking learning and how individual sequence elements contribute. The inclusion of short offline rest periods between learning epochs has been influential because it has revealed that a lot, if not most of the gains in behaviour (ie speed of finger movements) occur in these socalled micro-offline rest periods. The authors use a range of new decoding techniques, and exhaustively interrogate their data in different ways, using different decoding approaches. Regardless of the approach, impressively high decoding accuracies are observed, but when using a hybrid approach that combines the MEG data in different ways, the authors observe decoding accuracies of individual sequence elements from the MEG data of up to 94%.
We have previously showed that neural replay of MEG activity representing the practiced skill was prominent during rest intervals of early learning, and that the replay density correlated with micro-offline gains (Buch et al., 2021). These findings are consistent with recent reports (from two different research groups) that hippocampal ripple density increases during these inter-practice rest periods, and predict offline learning gains (Chen et al., 2024; Sjøgård et al., 2024). However, decoder performance in our earlier work (Buch et al., 2021) left room for improvement. Here, we reported a strategy to improve decoding accuracy that could benefit future studies of neural replay or BCI using MEG.
Weaknesses:
There are a few concerns which the authors may well be able to resolve. These are not weaknesses as such, but factors that would be helpful to address as these concern potential contributions to the results that one would like to rule out. Regarding the decoding results shown in Figure 2 etc, a concern is that within individual frequency bands, the highest accuracy seems to be within frequencies that match the rate of keypresses. This is a general concern when relating movement to brain activity, so is not specific to decoding as done here. As far as reported, there was no specific restraint to the arm or shoulder, and even then it is conceivable that small head movements would correlate highly with the vigor of individual finger movements. This concern is supported by the highest contribution in decoding accuracy being in middle frontal regions - midline structures that would be specifically sensitive to movement artefacts and don't seem to come to mind as key structures for very simple sequential keypress tasks such as this - and the overall pattern is remarkably symmetrical (despite being a unimanual finger task) and spatially broad. This issue may well be matching the time course of learning, as the vigor and speed of finger presses will also influence the degree to which the arm/shoulder and head move. This is not to say that useful information is contained within either of the frequencies or broadband data. But it raises the question of whether a lot is dominated by movement "artefacts" and one may get a more specific answer if removing any such contributions.
Reviewer #1 expresses concern that the combination of the low-frequency narrow-band decoder results, and the bilateral middle frontal regions displaying the highest average intra-parcel decoding performance across subjects is suggestive that the decoding results could be driven by head movement or other artefacts.
Head movement artefacts are highly unlikely to contribute meaningfully to our results for the following reasons. First, in addition to ICA denoising, all “recordings were visually inspected and marked to denoise segments containing other large amplitude artifacts due to movements” (see Methods). Second, the response pad was positioned in a manner that minimized wrist, arm or more proximal body movements during the task. Third, while online monitoring of head position was not performed for this study, it was assessed at the beginning and at the end of each recording. The head was restrained with an inflatable air bladder, and head movement between the beginning and end of each scan did not exceed 5mm for all participants included in the study.
The Reviewer states a concern that “it is conceivable that small head movements would correlate highly with the vigor of individual finger movements”. We agree that despite the steps taken above, it is possible that minor head movements could still contribute to some remaining variance in the MEG data in our study. However, such correlations between small head movements and finger movements could only meaningfully contribute to decoding performance if: (A) they were consistent and pervasive throughout the recording (which might not be the case if the head movements were related to movement vigor and vigor changed over time); and (B) they systematically varied between different finger movements, and also between the same finger movement performed at different sequence locations (see 5-class decoding performance in Figure 4B). The possibility of any head movement artefacts meeting all these conditions is unlikely. Alternatively, for this task design a much more likely confound could be the contribution of eye movement artefacts to the decoder performance (an issue raised by Reviewer #3 in the comments below).
Remember from Figure 1A in the manuscript that an asterisk marks the current position in the sequence and is updated at each keypress. Since participants make very few performance errors, the position of the asterisk on the display is highly correlated with the keypress being made in the sequence. Thus, it is possible that if participants are attending to the visual feedback provided on the display, they may generate eye movements that are systematically related to the task. Since we did record eye movements simultaneously with the MEG recordings (EyeLink 1000 Plus; Fs = 600 Hz), we were able to perform a control analysis to address this question. For each keypress event during trials in which no errors occurred (which is the same time-point that the asterisk position is updated), we extracted three features related to eye movements: 1) the gaze position at the time of asterisk position update (triggered by a KeyDown event), 2) the gaze position 150ms later, and 3) the peak velocity of the eye movement between the two positions. We then constructed a classifier from these features with the aim of predicting the location of the asterisk (ordinal positions 1-5) on the display. As shown in the confusion matrix below (Author response image 1), the classifier failed to perform above chance levels (overall cross-validated accuracy = 0.21817):
Author response image 1.
Confusion matrix showing that three eye movement features fail to predict asterisk position on the task display above chance levels (Fold 1 test accuracy = 0.21718; Fold 2 test accuracy = 0.22023; Fold 3 test accuracy = 0.21859; Fold 4 test accuracy = 0.22113; Fold 5 test accuracy = 0.21373; Overall cross-validated accuracy = 0.2181). Since the ordinal position of the asterisk on the display is highly correlated with the ordinal position of individual keypresses in the sequence, this analysis provides strong evidence that keypress decoding performance from MEG features is not explained by systematic relationships between finger movement behavior and eye movements (i.e. – behavioral artefacts) (end of figure legend).
Remember that the task display does not provide explicit feedback related to performance, only information about the present position in the sequence. Thus, it is possible that participants did not actively attend to the feedback. In fact, inspection of the eye position data revealed that on majority of trials, participants displayed random-walk-like gaze patterns around a central fixation point located near the center of the screen. Thus, participants did not attend to the asterisk position on the display, but instead intrinsically generated the action sequence. A similar realworld example would be manually inputting a long password into a secure online application. In this case, one intrinsically generates the sequence from memory and receives similar feedback about the password sequence position (also provided as asterisks) as provided in the study task – feedback which is typically ignored by the user.
The minimal participant engagement with the visual task display observed in this study highlights another important point – that the behavior in explicit sequence learning motor tasks is highly generative in nature rather than reactive to stimulus cues as in the serial reaction time task (SRTT). This is a crucial difference that must be carefully considered when designing investigations and comparing findings across studies.
We observed that initial keypress decoding accuracy was predominantly driven by contralateral primary sensorimotor cortex in the initial practice trials before transitioning to bilateral frontoparietal regions by trials 11 or 12 as performance gains plateaued. The contribution of contralateral primary sensorimotor areas to early skill learning has been extensively reported in humans and non-human animals.(Buch et al., 2021; Classen et al., 1998; Karni et al., 1995; Kleim et al., 1998) Similarly, the increased involvement of bilateral frontal and parietal regions to decoding during early skill learning in the non-dominant hand is well known. Enhanced bilateral activation in both frontal and parietal cortex during skill learning has been extensively reported (Doyon et al., 2002; Grafton et al., 1992; Hardwick et al., 2013; Kennerley et al., 2004; Shadmehr & Holcomb, 1997; Toni, Ramnani, et al., 2001), and appears to be even more prominent during early fine motor skill learning in the non-dominant hand (Lee et al., 2019; Sawamura et al., 2019). The frontal regions identified in these studies are known to play crucial roles in executive control (Battaglia-Mayer & Caminiti, 2019), motor planning (Toni, Thoenissen, et al., 2001), and working memory (Andersen & Buneo, 2002; Buneo & Andersen, 2006; Shadmehr & Holcomb, 1997; Toni, Ramnani, et al., 2001; Wolpert et al., 1998) processes, while the same parietal regions are known to integrate multimodal sensory feedback and support visuomotor transformations (Andersen & Buneo, 2002; Buneo & Andersen, 2006; Shadmehr & Holcomb, 1997; Toni, Ramnani, et al., 2001; Wolpert et al., 1998), in addition to working memory (Grover et al., 2022). Thus, it is not surprising that these regions increasingly contribute to decoding as subjects internalize the sequential task. We now include a statement reflecting these considerations in the revised Discussion.
A somewhat related point is this: when combining voxel and parcel space, a concern is whether a degree of circularity may have contributed to the improved accuracy of the combined data, because it seems to use the same MEG signals twice - the voxels most contributing are also those contributing most to a parcel being identified as relevant, as parcels reflect the average of voxels within a boundary. In this context, I struggled to understand the explanation given, ie that the improved accuracy of the hybrid model may be due to "lower spatially resolved whole-brain and higher spatially resolved regional activity patterns".
We disagree with the Reviewer’s assertion that the construction of the hybrid-space decoder is circular for the following reasons. First, the base feature set for the hybrid-space decoder constructed for all participants includes whole-brain spatial patterns of MEG source activity averaged within parcels. As stated in the manuscript, these 148 inter-parcel features reflect “lower spatially resolved whole-brain activity patterns” or global brain dynamics. We then independently test how well spatial patterns of MEG source activity for all voxels distributed within individual parcels can decode keypress actions. Again, the testing of these intra-parcel spatial patterns, intended to capture “higher spatially resolved regional brain activity patterns”, is completely independent from one another and independent from the weighting of individual inter-parcel features. These intra-parcel features could, for example, provide additional information about muscle activation patterns or the task environment. These approximately 1150 intra-parcel voxels (on average, within the total number varying between subjects) are then combined with the 148 inter-parcel features to construct the final hybrid-space decoder. In fact, this varied spatial filter approach shares some similarities to the construction of convolutional neural networks (CNNs) used to perform object recognition in image classification applications (Srinivas et al., 2016). One could also view this hybrid-space decoding approach as a spatial analogue to common timefrequency based analyses such as theta-gamma phase amplitude coupling (θ/γ PAC), which assess interactions between two or more narrow-band spectral features derived from the same time-series data (Lisman & Jensen, 2013).
We directly tested this hypothesis – that spatially overlapping intra- and inter-parcel features portray different information – by constructing an alternative hybrid-space decoder (Hybrid<sub>Alt</sub>) that excluded average inter-parcel features which spatially overlapped with intra-parcel voxel features, and comparing the performance to the decoder used in the manuscript (Hybrid<sub>Orig</sub>). The prediction was that if the overlapping parcel contained similar information to the more spatially resolved voxel patterns, then removing the parcel features (n=8) from the decoding analysis should not impact performance. In fact, despite making up less than 1% of the overall input feature space, removing those parcels resulted in a significant drop in overall performance greater than 2% (78.15% ± 7.03% SD for Hybrid<sub>Orig</sub> vs. 75.49% ± 7.17% for Hybrid<sub>Alt</sub>; Wilcoxon signed rank test, z = 3.7410, p = 1.8326e-04; Author response image 2).
Author response image 2.
Comparison of decoding performances with two different hybrid approaches. Hybrid<sub>Alt</sub>: Intra-parcel voxel-space features of top ranked parcels and inter-parcel features of remaining parcels. Hybrid<sub>Orig</sub>: Voxel-space features of top ranked parcels and whole-brain parcel-space features (i.e. – the version used in the manuscript). Dots represent decoding accuracy for individual subjects. Dashed lines indicate the trend in performance change across participants. Note, that Hybrid<sub>Orig</sub> (the approach used in our manuscript) significantly outperforms the Hybrid<sub>Alt</sub> approach, indicating that the excluded parcel features provide unique information compared to the spatially overlapping intra-parcel voxel patterns (end of figure legend).
Firstly, there will be a relatively high degree of spatial contiguity among voxels because of the nature of the signal measured, i.e. nearby individual voxels are unlikely to be independent. Secondly, the voxel data gives a somewhat misleading sense of precision; the inversion can be set up to give an estimate for each voxel, but there will not just be dependence among adjacent voxels, but also substantial variation in the sensitivity and confidence with which activity can be projected to different parts of the brain. Midline and deeper structures come to mind, where the inversion will be more problematic than for regions along the dorsal convexity of the brain, and a concern is that in those midline structures, the highest decoding accuracy is seen.
We agree with the Reviewer that some inter-parcel features representing neighboring (or spatially contiguous) voxels are likely to be correlated, an important confound in connectivity analyses (Colclough et al., 2015; Colclough et al., 2016), not performed in our investigation.
In our study, correlations between adjacent voxels effectively reduce the dimensionality of the input feature space. However, as long as there are multiple groups of correlated voxels within each parcel (i.e. – the rank is greater than 1), the intra-parcel spatial patterns could meaningfully contribute to the decoder performance, as shown by the following results:
First, we obtained higher decoding accuracy with voxel-space features (74.51% ± 7.34% SD) compared to parcel space features (68.77% ± 7.6%; Figure 3B), indicating individual voxels carry more information in decoding the keypresses than the averaged voxel-space features or parcel space features. Second, individual voxels within a parcel showed varying feature importance scores in decoding keypresses (Author response image 3). This finding shows that correlated voxels form mini subclusters that are much smaller spatially than the parcel they reside within.
Author response image 3.:
Feature importance score of individual voxels in decoding keypresses: MRMR was used to rank the individual voxel space features in decoding keypresses and the min-max normalized MRMR score was mapped to a structural brain surface. Note that individual voxels within a parcel showed different contribution to decoding (end of figure legend).
Some of these concerns could be addressed by recording head movement (with enough precision) to regress out these contributions. The authors state that head movement was monitored with 3 fiducials, and their time courses ought to provide a way to deal with this issue. The ICA procedure may not have sufficiently dealt with removing movement-related problems, but one could eg relate individual components that were identified to the keypresses as another means for checking. An alternative could be to focus on frequency ranges above the movement frequencies. The accuracy for those still seems impressive and may provide a slightly more biologically plausible assessment.
We have already addressed the issue of movement related artefacts in the first response above. With respect to a focus on frequency ranges above movement frequencies, the Reviewer states the “accuracy for those still seems impressive and may provide a slightly more biologically plausible assessment”. First, it is important to note that cortical delta-band oscillations measured with local field potentials (LFPs) in macaques is known to contain important information related to end-effector kinematics (Bansal et al., 2011; Mollazadeh et al., 2011) muscle activation patterns (Flint et al., 2012) and temporal sequencing (Churchland et al., 2012) during skilled reaching and grasping actions. Thus, there is a substantial body of evidence that low-frequency neural oscillatory activity in this range contains important information about the skill learning behavior investigated in the present study. Second, our own data shows (which the Reviewer also points out) that significant information related to the skill learning behavior is also present in higher frequency bands (see Figure 2A and Figure 3—figure supplement 1). As we pointed out in our earlier response to questions about the hybrid space decoder architecture (see above), it is likely that different, yet complimentary, information is encoded across different temporal frequencies (just as it is encoded across different spatial frequencies) (Heusser et al., 2016). Again, this interpretation is supported by our data as the highest performing classifiers in all cases (when holding all parameters constant) were always constructed from broadband input MEG data (Figure 2A and Figure 3—figure supplement 1).
One question concerns the interpretation of the results shown in Figure 4. They imply that during the course of learning, entirely different brain networks underpin the behaviour. Not only that, but they also include regions that would seem rather unexpected to be key nodes for learning and expressing relatively simple finger sequences, such as here. What then is the biological plausibility of these results? The authors seem to circumnavigate this issue by moving into a distance metric that captures the (neural network) changes over the course of learning, but the discussion seems detached from which regions are actually involved; or they offer a rather broad discussion of the anatomical regions identified here, eg in the context of LFOs, where they merely refer to "frontoparietal regions".
The Reviewer notes the shift in brain networks driving keypress decoding performance between trials 1, 11 and 36 as shown in Figure 4A. The Reviewer questions whether these shifts in brain network states underpinning the skill are biologically plausible, as well as the likelihood that bilateral superior and middle frontal and parietal cortex are important nodes within these networks.
First, previous fMRI work in humans assessed changes in functional connectivity patterns while participants performed a similar sequence learning task to our present study (Bassett et al., 2011). Using a dynamic network analysis approach, Bassett et al. showed that flexibility in the composition of individual network modules (i.e. – changes in functional brain region membership of orthogonal brain networks) is up-regulated in novel learning environments and explains differences in learning rates across individuals. Thus, consistent with our findings, it is likely that functional brain networks rapidly reconfigure during early learning of novel sequential motor skills.
Second, frontoparietal network activity is known to support motor memory encoding during early learning (Albouy et al., 2013; Albouy et al., 2012). For example, reactivation events in the posterior parietal (Qin et al., 1997) and medial prefrontal (Euston et al., 2007; Molle & Born, 2009) cortex (MPFC) have been temporally linked to hippocampal replay, and are posited to support memory consolidation across several memory domains (Frankland & Bontempi, 2005), including motor sequence learning (Albouy et al., 2015; Buch et al., 2021; F. Jacobacci et al., 2020). Further, synchronized interactions between MPFC and hippocampus are more prominent during early as opposed to later learning stages (Albouy et al., 2013; Gais et al., 2007; Sterpenich et al., 2009), perhaps reflecting “redistribution of hippocampal memories to MPFC” (Albouy et al., 2013). MPFC contributes to very early memory formation by learning association between contexts, locations, events and adaptive responses during rapid learning (Euston et al., 2012). Consistently, coupling between hippocampus and MPFC has been shown during initial memory encoding and during subsequent rest (van Kesteren et al., 2010; van Kesteren et al., 2012). Importantly, MPFC activity during initial memory encoding predicts subsequent recall (Wagner et al., 1998). Thus, the spatial map required to encode a motor sequence memory may be “built under the supervision of the prefrontal cortex” (Albouy et al., 2012), also engaged in the development of an abstract representation of the sequence (Ashe et al., 2006). In more abstract terms, the prefrontal, premotor and parietal cortices support novice performance “by deploying attentional and control processes” (Doyon et al., 2009; Hikosaka et al., 2002; Penhune & Steele, 2012) required during early learning (Doyon et al., 2009; Hikosaka et al., 2002; Penhune & Steele, 2012). The dorsolateral prefrontal cortex DLPFC specifically is thought to engage in goal selection and sequence monitoring during early skill practice (Schendan et al., 2003), all consistent with the schema model of declarative memory in which prefrontal cortices play an important role in encoding (Morris, 2006; Tse et al., 2007). Thus, several prefrontal and frontoparietal regions contributing to long term learning (Berlot et al., 2020) are also engaged in early stages of encoding. Altogether, there is strong biological support for the involvement of bilateral prefrontal and frontoparietal regions to decoding during early skill learning. We now address this issue in the revised manuscript.
If I understand correctly, the offline neural representation analysis is in essence the comparison of the last keypress vs the first keypress of the next sequence. In that sense, the activity during offline rest periods is actually not considered. This makes the nomenclature somewhat confusing. While it matches the behavioural analysis, having only key presses one can't do it in any other way, but here the authors actually do have recordings of brain activity during offline rest. So at the very least calling it offline neural representation is misleading to this reviewer because what is compared is activity during the last and during the next keypress, not activity during offline periods. But it also seems a missed opportunity - the authors argue that most of the relevant learning occurs during offline rest periods, yet there is no attempt to actually test whether activity during this period can be useful for the questions at hand here.
We agree with the Reviewer that our previous “offline neural representation” nomenclature could be misinterpreted. In the revised manuscript we refer to this difference as the “offline neural representational change”. Please, note that our previous work did link offline neural activity (i.e. – 16-22 Hz beta power (Bonstrup et al., 2019) and neural replay density (Buch et al., 2021) during inter-practice rest periods) to observed micro-offline gains.
Reviewer #2 (Public review):
Summary
Dash et al. asked whether and how the neural representation of individual finger movements is "contextualized" within a trained sequence during the very early period of sequential skill learning by using decoding of MEG signal. Specifically, they assessed whether/how the same finger presses (pressing index finger) embedded in the different ordinal positions of a practiced sequence (4-1-3-2-4; here, the numbers 1 through 4 correspond to the little through the index fingers of the non-dominant left hand) change their representation (MEG feature). They did this by computing either the decoding accuracy of the index finger at the ordinal positions 1 vs. 5 (index_OP1 vs index_OP5) or pattern distance between index_OP1 vs. index_OP5 at each training trial and found that both the decoding accuracy and the pattern distance progressively increase over the course of learning trials. More interestingly, they also computed the pattern distance for index_OP5 for the last execution of a practice trial vs. index_OP1 for the first execution in the next practice trial (i.e., across the rest period). This "off-line" distance was significantly larger than the "on-line" distance, which was computed within practice trials and predicted micro-offline skill gain. Based on these results, the authors conclude that the differentiation of representation for the identical movement embedded in different positions of a sequential skill ("contextualization") primarily occurs during early skill learning, especially during rest, consistent with the recent theory of the "micro-offline learning" proposed by the authors' group. I think this is an important and timely topic for the field of motor learning and beyond.
Strengths
The specific strengths of the current work are as follows. First, the use of temporally rich neural information (MEG signal) has a large advantage over previous studies testing sequential representations using fMRI. This allowed the authors to examine the earliest period (= the first few minutes of training) of skill learning with finer temporal resolution. Second, through the optimization of MEG feature extraction, the current study achieved extremely high decoding accuracy (approx. 94%) compared to previous works. As claimed by the authors, this is one of the strengths of the paper (but see my comments). Third, although some potential refinement might be needed, comparing "online" and "offline" pattern distance is a neat idea.
Weaknesses
Along with the strengths I raised above, the paper has some weaknesses. First, the pursuit of high decoding accuracy, especially the choice of time points and window length (i.e., 200 msec window starting from 0 msec from key press onset), casts a shadow on the interpretation of the main result. Currently, it is unclear whether the decoding results simply reflect behavioral change or true underlying neural change. As shown in the behavioral data, the key press speed reached 3~4 presses per second already at around the end of the early learning period (11th trial), which means inter-press intervals become as short as 250-330 msec. Thus, in almost more than 60% of training period data, the time window for MEG feature extraction (200 msec) spans around 60% of the inter-press intervals. Considering that the preparation/cueing of subsequent presses starts ahead of the actual press (e.g., Kornysheva et al., 2019) and/or potential online planning (e.g., Ariani and Diedrichsen, 2019), the decoder likely has captured these future press information as well as the signal related to the current key press, independent of the formation of genuine sequential representation (e.g., "contextualization" of individual press). This may also explain the gradual increase in decoding accuracy or pattern distance between index_OP1 vs. index_OP5 (Figure 4C and 5A), which co-occurred with performance improvement, as shorter inter-press intervals are more favorable for the dissociating the two index finger presses followed by different finger presses. The compromised decoding accuracies for the control sequences can be explained in similar logic. Therefore, more careful consideration and elaborated discussion seem necessary when trying to both achieve high-performance decoding and assess early skill learning, as it can impact all the subsequent analyses.
The Reviewer raises the possibility that (given the windowing parameters used in the present study) an increase in “contextualization” with learning could simply reflect faster typing speeds as opposed to an actual change in the underlying neural representation.
We now include a new control analysis that addresses this issue as well as additional re-examination of previously reported results with respect to this issue – all of which are inconsistent with this alternative explanation that “contextualization” reflects a change in mixing of keypress related MEG features as opposed to a change in the underlying representations themselves. As correct sequences are generated at higher and higher speeds over training, MEG activity patterns related to the planning, execution, evaluation and memory of individual keypresses overlap more in time. Thus, increased overlap between the “4” and “1” keypresses (at the start of the sequence) and “2” and “4” keypresses (at the end of the sequence) could artefactually increase contextualization distances even if the underlying neural representations for the individual keypresses remain unchanged. One must also keep in mind that since participants repeat the sequence multiple times within the same trial, a majority of the index finger keypresses are performed adjacent to one another (i.e. - the “4-4” transition marking the end of one sequence and the beginning of the next). Thus, increased overlap between consecutive index finger keypresses as typing speed increased should increase their similarity and mask contextualization related changes to the underlying neural representations.
We addressed this question by conducting a new multivariate regression analysis to directly assess whether the neural representation distance score could be predicted by the 4-1, 2-4 and 4-4 keypress transition times observed for each complete correct sequence (both predictor and response variables were z-score normalized within-subject). The results of this analysis also affirmed that the possible alternative explanation that contextualization effects are simple reflections of increased mixing is not supported by the data (Adjusted R<sup>2</sup> = 0.00431; F = 5.62). We now include this new negative control analysis in the revised manuscript.
We also re-examined our previously reported classification results with respect to this issue. We reasoned that if mixing effects reflecting the ordinal sequence structure is an important driver of the contextualization finding, these effects should be observable in the distribution of decoder misclassifications. For example, “4” keypresses would be more likely to be misclassified as “1” or “2” keypresses (or vice versa) than as “3” keypresses. The confusion matrices presented in Figures 3C and 4B and Figure 3—figure supplement 3A display a distribution of misclassifications that is inconsistent with an alternative mixing effect explanation of contextualization.
Based upon the increased overlap between adjacent index finger keypresses (i.e. – “4-4” transition), we also reasoned that the decoder tasked with separating individual index finger keypresses into two distinct classes based upon sequence position, should show decreased performance as typing speed increases. However, Figure 4C in our manuscript shows that this is not the case. The 2-class hybrid classifier actually displays improved classification performance over early practice trials despite greater temporal overlap. Again, this is inconsistent with the idea that the contextualization effect simply reflects increased mixing of individual keypress features.
In summary, both re-examination of previously reported data and new control analyses all converged on the idea that the proximity between keypresses does not explain contextualization.
We do agree with the Reviewer that the naturalistic, generative, self-paced task employed in the present study results in overlapping brain processes related to planning, execution, evaluation and memory of the action sequence. We also agree that there are several tradeoffs to consider in the construction of the classifiers depending on the study aim. Given our aim of optimizing keypress decoder accuracy in the present study, the set of trade-offs resulted in representations reflecting more the latter three processes, and less so the planning component. Whether separate decoders can be constructed to tease apart the representations or networks supporting these overlapping processes is an important future direction of research in this area. For example, work presently underway in our lab constrains the selection of windowing parameters in a manner that allows individual classifiers to be temporally linked to specific planning, execution, evaluation or memory-related processes to discern which brain networks are involved and how they adaptively reorganize with learning. Results from the present study (Figure 4—figure supplement 2) showing hybrid-space decoder prediction accuracies exceeding 74% for temporal windows spanning as little as 25ms and located up to 100ms prior to the KeyDown event strongly support the feasibility of such an approach.
Related to the above point, testing only one particular sequence (4-1-3-2-4), aside from the control ones, limits the generalizability of the finding. This also may have contributed to the extremely high decoding accuracy reported in the current study.
The Reviewer raises a question about the generalizability of the decoder accuracy reported in our study. Fortunately, a comparison between decoder performances on Day 1 and Day 2 datasets does provide insight into this issue. As the Reviewer points out, the classifiers in this study were trained and tested on keypresses performed while practicing a specific sequence (4-1-3-2-4). The study was designed this way as to avoid the impact of interference effects on learning dynamics. The cross-validated performance of classifiers on MEG data collected within the same session was 90.47% overall accuracy (4-class; Figure 3C). We then tested classifier performance on data collected during a separate MEG session conducted approximately 24 hours later (Day 2; see Figure 3 — figure supplement 3). We observed a reduction in overall accuracy rate to 87.11% when tested on MEG data recorded while participants performed the same learned sequence, and 79.44% when they performed several previously unpracticed sequences. Both changes in accuracy are important with regards to the generalizability of our findings. First, 87.11% performance accuracy for the trained sequence data on Day 2 (a reduction of only 3.36%) indicates that the hybrid-space decoder performance is robust over multiple MEG sessions, and thus, robust to variations in SNR across the MEG sensor array caused by small differences in head position between scans. This indicates a substantial advantage over sensor-space decoding approaches. Furthermore, when tested on data from unpracticed sequences, overall performance dropped an additional 7.67%. This difference reflects the performance bias of the classifier for the trained sequence, possibly caused by high-order sequence structure being incorporated into the feature weights. In the future, it will be important to understand in more detail how random or repeated keypress sequence training data impacts overall decoder performance and generalization. We strongly agree with the Reviewer that the issue of generalizability is extremely important and have added a new paragraph to the Discussion in the revised manuscript highlighting the strengths and weaknesses of our study with respect to this issue.
In terms of clinical BCI, one of the potential relevance of the study, as claimed by the authors, it is not clear that the specific time window chosen in the current study (up to 200 msec since key press onset) is really useful. In most cases, clinical BCI would target neural signals with no overt movement execution due to patients' inability to move (e.g., Hochberg et al., 2012). Given the time window, the surprisingly high performance of the current decoder may result from sensory feedback and/or planning of subsequent movement, which may not always be available in the clinical BCI context. Of course, the decoding accuracy is still much higher than chance even when using signal before the key press (as shown in Figure 4 Supplement 2), but it is not immediately clear to me that the authors relate their high decoding accuracy based on post-movement signal to clinical BCI settings.
The Reviewer questions the relevance of the specific window parameters used in the present study for clinical BCI applications, particularly for paretic patients who are unable to produce finger movements or for whom afferent sensory feedback is no longer intact. We strongly agree with the Reviewer that any intended clinical application must carefully consider the specific input feature constraints dictated by the clinical cohort, and in turn impose appropriate and complimentary constraints on classifier parameters that may differ from the ones used in the present study. We now highlight this issue in the Discussion of the revised manuscript and relate our present findings to published clinical BCI work within this context.
One of the important and fascinating claims of the current study is that the "contextualization" of individual finger movements in a trained sequence specifically occurs during short rest periods in very early skill learning, echoing the recent theory of micro-offline learning proposed by the authors' group. Here, I think two points need to be clarified. First, the concept of "contextualization" is kept somewhat blurry throughout the text. It is only at the later part of the Discussion (around line #330 on page 13) that some potential mechanism for the "contextualization" is provided as "what-and-where" binding. Still, it is unclear what "contextualization" actually is in the current data, as the MEG signal analyzed is extracted from 0-200 msec after the keypress. If one thinks something is contextualizing an action, that contextualization should come earlier than the action itself.
The Reviewer requests that we: 1) more clearly define our use of the term “contextualization” and 2) provide the rationale for assessing it over a 200ms window aligned to the KeyDown event. This choice of window parameters means that the MEG activity used in our analysis was coincident with, rather than preceding, the actual keypresses. We define contextualization as the differentiation of representation for the identical movement embedded in different positions of a sequential skill. That is, representations of individual action elements progressively incorporate information about their relationship to the overall sequence structure as the skill is learned. We agree with the Reviewer that this can be appropriately interpreted as “what-and-where” binding. We now incorporate this definition in the Introduction of the revised manuscript as requested.
The window parameters for optimizing accurate decoding individual finger movements were determined using a grid search of the parameter space (a sliding window of variable width between 25-350 ms with 25 ms increments variably aligned from 0 to +100ms with 10ms increments relative to the KeyDown event). This approach generated 140 different temporal windows for each keypress for each participant, with the final parameter selection determined through comparison of the resulting performance between each decoder. Importantly, the decision to optimize for decoding accuracy placed an emphasis on keypress representations characterized by the most consistent and robust features shared across subjects, which in turn maximize statistical power in detecting common learning-related changes. In this case, the optimal window encompassed a 200ms epoch aligned to the KeyDown event (t<sub>0</sub> = 0 ms). We then asked if the representations (i.e. – spatial patterns of combined parcel- and voxel-space activity) of the same digit at two different sequence positions changed with practice within this optimal decoding window. Of course, our findings do not rule out the possibility that contextualization can also be found before or even after this time window, as we did not directly address this issue in the present study. Future work in our lab, as pointed out above, are investigating contextualization within different time windows tailored specifically for assessing sequence skill action planning, execution, evaluation and memory processes.
The second point is that the result provided by the authors is not yet convincing enough to support the claim that "contextualization" occurs during rest. In the original analysis, the authors presented the statistical significance regarding the correlation between the "offline" pattern differentiation and micro-offline skill gain (Figure 5. Supplement 1), as well as the larger "offline" distance than "online" distance (Figure 5B). However, this analysis looks like regressing two variables (monotonically) increasing as a function of the trial. Although some information in this analysis, such as what the independent/dependent variables were or how individual subjects were treated, was missing in the Methods, getting a statistically significant slope seems unsurprising in such a situation. Also, curiously, the same quantitative evidence was not provided for its "online" counterpart, and the authors only briefly mentioned in the text that there was no significant correlation between them. It may be true looking at the data in Figure 5A as the online representation distance looks less monotonically changing, but the classification accuracy presented in Figure 4C, which should reflect similar representational distance, shows a more monotonic increase up to the 11th trial. Further, the ways the "online" and "offline" representation distance was estimated seem to make them not directly comparable. While the "online" distance was computed using all the correct press data within each 10 sec of execution, the "offline" distance is basically computed by only two presses (i.e., the last index_OP5 vs. the first index_OP1 separated by 10 sec of rest). Theoretically, the distance between the neural activity patterns for temporally closer events tends to be closer than that between the patterns for temporally far-apart events. It would be fairer to use the distance between the first index_OP1 vs. the last index_OP5 within an execution period for "online" distance, as well.
The Reviewer suggests that the current data is not enough to show that contextualization occurs during rest and raises two important concerns: 1) the relationship between online contextualization and micro-online gains is not shown, and 2) the online distance was calculated differently from its offline counterpart (i.e. - instead of calculating the distance between last Index<sub>OP5</sub> and first Index<sub>OP1</sub> from a single trial, the distance was calculated for each sequence within a trial and then averaged).
We addressed the first concern by performing individual subject correlations between 1) contextualization changes during rest intervals and micro-offline gains; 2) contextualization changes during practice trials and micro-online gains, and 3) contextualization changes during practice trials and micro-offline gains (Figure 5 – figure supplement 4). We then statistically compared the resulting correlation coefficient distributions and found that within-subject correlations for contextualization changes during rest intervals and micro-offline gains were significantly higher than online contextualization and micro-online gains (t = 3.2827, p = 0.0015) and online contextualization and micro-offline gains (t = 3.7021, p = 5.3013e-04). These results are consistent with our interpretation that micro-offline gains are supported by contextualization changes during the inter-practice rest periods.
With respect to the second concern, we agree with the Reviewer that one limitation of the analysis comparing online versus offline changes in contextualization as presented in the original manuscript, is that it does not eliminate the possibility that any differences could simply be explained by the passage of time (which is smaller for the online analysis compared to the offline analysis). The Reviewer suggests an approach that addresses this issue, which we have now carried out. When quantifying online changes in contextualization from the first Index<sub>OP1</sub> the last Index<sub>OP5</sub> keypress in the same trial we observed no learning-related trend (Figure 5 – figure supplement 5, right panel). Importantly, offline distances were significantly larger than online distances regardless of the measurement approach and neither predicted online learning (Figure 5 – figure supplement 6).
A related concern regarding the control analysis, where individual values for max speed and the degree of online contextualization were compared (Figure 5 Supplement 3), is whether the individual difference is meaningful. If I understood correctly, the optimization of the decoding process (temporal window, feature inclusion/reduction, decoder, etc.) was performed for individual participants, and the same feature extraction was also employed for the analysis of representation distance (i.e., contextualization). If this is the case, the distances are individually differently calculated and they may need to be normalized relative to some stable reference (e.g., 1 vs. 4 or average distance within the control sequence presses) before comparison across the individuals.
The Reviewer makes a good point here. We have now implemented the suggested normalization procedure in the analysis provided in the revised manuscript.
Reviewer #3 (Public review):
Summary:
One goal of this paper is to introduce a new approach for highly accurate decoding of finger movements from human magnetoencephalography data via dimension reduction of a "multiscale, hybrid" feature space. Following this decoding approach, the authors aim to show that early skill learning involves "contextualization" of the neural coding of individual movements, relative to their position in a sequence of consecutive movements. Furthermore, they aim to show that this "contextualization" develops primarily during short rest periods interspersed with skill training and correlates with a performance metric which the authors interpret as an indicator of offline learning.
Strengths:
A clear strength of the paper is the innovative decoding approach, which achieves impressive decoding accuracies via dimension reduction of a "multi-scale, hybrid space". This hybrid-space approach follows the neurobiologically plausible idea of the concurrent distribution of neural coding across local circuits as well as large-scale networks. A further strength of the study is the large number of tested dimension reduction techniques and classifiers (though the manuscript reveals little about the comparison of the latter).
We appreciate the Reviewer’s comments regarding the paper’s strengths.
A simple control analysis based on shuffled class labels could lend further support to this complex decoding approach. As a control analysis that completely rules out any source of overfitting, the authors could test the decoder after shuffling class labels. Following such shuffling, decoding accuracies should drop to chance level for all decoding approaches, including the optimized decoder. This would also provide an estimate of actual chance-level performance (which is informative over and beyond the theoretical chance level). Furthermore, currently, the manuscript does not explain the huge drop in decoding accuracies for the voxel-space decoding (Figure 3B). Finally, the authors' approach to cortical parcellation raises questions regarding the information carried by varying dipole orientations within a parcel (which currently seems to be ignored?) and the implementation of the mean-flipping method (given that there are two dimensions - space and time - what do the authors refer to when they talk about the sign of the "average source", line 477?).
The Reviewer recommends that we: 1) conduct an additional control analysis on classifier performance using shuffled class labels, 2) provide a more detailed explanation regarding the drop in decoding accuracies for the voxel-space decoding following LDA dimensionality reduction (see Fig 3B), and 3) provide additional details on how problems related to dipole solution orientations were addressed in the present study.
In relation to the first point, we have now implemented a random shuffling approach as a control for the classification analyses. The results of this analysis indicated that the chance level accuracy was 22.12% (± SD 9.1%) for individual keypress decoding (4-class classification), and 18.41% (± SD 7.4%) for individual sequence item decoding (5-class classification), irrespective of the input feature set or the type of decoder used. Thus, the decoding accuracy observed with the final model was substantially higher than these chance levels.
Second, please note that the dimensionality of the voxel-space feature set is very high (i.e. – 15684). LDA attempts to map the input features onto a much smaller dimensional space (number of classes – 1; e.g. – 3 dimensions, for 4-class keypress decoding). Given the very high dimension of the voxel-space input features in this case, the resulting mapping exhibits reduced accuracy. Despite this general consideration, please refer to Figure 3—figure supplement 3, where we observe improvement in voxel-space decoder performance when utilizing alternative dimensionality reduction techniques.
The decoders constructed in the present study assess the average spatial patterns across time (as defined by the windowing procedure) in the input feature space. We now provide additional details in the Methods of the revised manuscript pertaining to the parcellation procedure and how the sign ambiguity problem was addressed in our analysis.
Weaknesses:
A clear weakness of the paper lies in the authors' conclusions regarding "contextualization". Several potential confounds, described below, question the neurobiological implications proposed by the authors and provide a simpler explanation of the results. Furthermore, the paper follows the assumption that short breaks result in offline skill learning, while recent evidence, described below, casts doubt on this assumption.
We thank the Reviewer for giving us the opportunity to address these issues in detail (see below).
The authors interpret the ordinal position information captured by their decoding approach as a reflection of neural coding dedicated to the local context of a movement (Figure 4). One way to dissociate ordinal position information from information about the moving effectors is to train a classifier on one sequence and test the classifier on other sequences that require the same movements, but in different positions (Kornysheva et al., 2019). In the present study, however, participants trained to repeat a single sequence (4-1-3-2-4). As a result, ordinal position information is potentially confounded by the fixed finger transitions around each of the two critical positions (first and fifth press). Across consecutive correct sequences, the first keypress in a given sequence was always preceded by a movement of the index finger (=last movement of the preceding sequence), and followed by a little finger movement. The last keypress, on the other hand, was always preceded by a ring finger movement, and followed by an index finger movement (=first movement of the next sequence). Figure 4 - Supplement 2 shows that finger identity can be decoded with high accuracy (>70%) across a large time window around the time of the key press, up to at least +/-100 ms (and likely beyond, given that decoding accuracy is still high at the boundaries of the window depicted in that figure). This time window approaches the keypress transition times in this study. Given that distinct finger transitions characterized the first and fifth keypress, the classifier could thus rely on persistent (or "lingering") information from the preceding finger movement, and/or "preparatory" information about the subsequent finger movement, in order to dissociate the first and fifth keypress. Currently, the manuscript provides no evidence that the context information captured by the decoding approach is more than a by-product of temporally extended, and therefore overlapping, but independent neural representations of consecutive keypresses that are executed in close temporal proximity - rather than a neural representation dedicated to context.
Such temporal overlap of consecutive, independent finger representations may also account for the dynamics of "ordinal coding"/"contextualization", i.e., the increase in 2-class decoding accuracy, across Day 1 (Figure 4C). As learning progresses, both tapping speed and the consistency of keypress transition times increase (Figure 1), i.e., consecutive keypresses are closer in time, and more consistently so. As a result, information related to a given keypress is increasingly overlapping in time with information related to the preceding and subsequent keypresses. The authors seem to argue that their regression analysis in Figure 5 - Figure Supplement 3 speaks against any influence of tapping speed on "ordinal coding" (even though that argument is not made explicitly in the manuscript). However, Figure 5 - Figure Supplement 3 shows inter-individual differences in a between-subject analysis (across trials, as in panel A, or separately for each trial, as in panel B), and, therefore, says little about the within-subject dynamics of "ordinal coding" across the experiment. A regression of trial-by-trial "ordinal coding" on trial-by-trial tapping speed (either within-subject or at a group-level, after averaging across subjects) could address this issue. Given the highly similar dynamics of "ordinal coding" on the one hand (Figure 4C), and tapping speed on the other hand (Figure 1B), I would expect a strong relationship between the two in the suggested within-subject (or group-level) regression. Furthermore, learning should increase the number of (consecutively) correct sequences, and, thus, the consistency of finger transitions. Therefore, the increase in 2-class decoding accuracy may simply reflect an increasing overlap in time of increasingly consistent information from consecutive keypresses, which allows the classifier to dissociate the first and fifth keypress more reliably as learning progresses, simply based on the characteristic finger transitions associated with each. In other words, given that the physical context of a given keypress changes as learning progresses - keypresses move closer together in time and are more consistently correct - it seems problematic to conclude that the mental representation of that context changes. To draw that conclusion, the physical context should remain stable (or any changes to the physical context should be controlled for).
The issues raised by Reviewer #3 here are similar to two issues raised by Reviewer #2 above. We agree they must both be carefully considered in any evaluation of our findings.
As both Reviewers pointed out, the classifiers in this study were trained and tested on keypresses performed while practicing a specific sequence (4-1-3-2-4). The study was designed this way as to avoid the impact of interference effects on learning dynamics. The cross-validated performance of classifiers on MEG data collected within the same session was 90.47% overall accuracy (4class; Figure 3C). We then tested classifier performance on data collected during a separate MEG session conducted approximately 24 hours later (Day 2; see Figure 3—supplement 3). We observed a reduction in overall accuracy rate to 87.11% when tested on MEG data recorded while participants performed the same learned sequence, and 79.44% when they performed several previously unpracticed sequences. This classification performance difference of 7.67% when tested on the Day 2 data could reflect the performance bias of the classifier for the trained sequence, possibly caused by mixed information from temporally close keypresses being incorporated into the feature weights.
Along these same lines, both Reviewers also raise the possibility that an increase in “ordinal coding/contextualization” with learning could simply reflect an increase in this mixing effect caused by faster typing speeds as opposed to an actual change in the underlying neural representation. The basic idea is that as correct sequences are generated at higher and higher speeds over training, MEG activity patterns related to the planning, execution, evaluation and memory of individual keypresses overlap more in time. Thus, increased overlap between the “4” and “1” keypresses (at the start of the sequence) and “2” and “4” keypresses (at the end of the sequence) could artefactually increase contextualization distances even if the underlying neural representations for the individual keypresses remain unchanged (assuming this mixing of representations is used by the classifier to differentially tag each index finger press). If this were the case, it follows that such mixing effects reflecting the ordinal sequence structure would also be observable in the distribution of decoder misclassifications. For example, “4” keypresses would be more likely to be misclassified as “1” or “2” keypresses (or vice versa) than as “3” keypresses. The confusion matrices presented in Figures 3C and 4B and Figure 3—figure supplement 3A in the previously submitted manuscript do not show this trend in the distribution of misclassifications across the four fingers.
Following this logic, it’s also possible that if the ordinal coding is largely driven by this mixing effect, the increased overlap between consecutive index finger keypresses during the 4-4 transition marking the end of one sequence and the beginning of the next one could actually mask contextualization-related changes to the underlying neural representations and make them harder to detect. In this case, a decoder tasked with separating individual index finger keypresses into two distinct classes based upon sequence position might show decreased performance with learning as adjacent keypresses overlapped in time with each other to an increasing extent. However, Figure 4C in our previously submitted manuscript does not support this possibility, as the 2-class hybrid classifier displays improved classification performance over early practice trials despite greater temporal overlap.
As noted in the above reply to Reviewer #2, we also conducted a new multivariate regression analysis to directly assess whether the neural representation distance score could be predicted by the 4-1, 2-4 and 4-4 keypress transition times observed for each complete correct sequence (both predictor and response variables were z-score normalized within-subject). The results of this analysis affirmed that the possible alternative explanation put forward by the Reviewer is not supported by our data (Adjusted R<sup>2</sup> = 0.00431; F = 5.62). We now include this new negative control analysis result in the revised manuscript.
Finally, the Reviewer hints that one way to address this issue would be to compare MEG responses before and after learning for sequences typed at a fixed speed. However, given that the speed-accuracy trade-off should improve with learning, a comparison between unlearned and learned skill states would dictate that the skill be evaluated at a very low fixed speed. Essentially, such a design presents the problem that the post-training test is evaluating the representation in the unlearned behavioral state that is not representative of the acquired skill. Thus, this approach would miss most learning effects on a task in which speed is the main learning metrics.
A similar difference in physical context may explain why neural representation distances ("differentiation") differ between rest and practice (Figure 5). The authors define "offline differentiation" by comparing the hybrid space features of the last index finger movement of a trial (ordinal position 5) and the first index finger movement of the next trial (ordinal position 1). However, the latter is not only the first movement in the sequence but also the very first movement in that trial (at least in trials that started with a correct sequence), i.e., not preceded by any recent movement. In contrast, the last index finger of the last correct sequence in the preceding trial includes the characteristic finger transition from the fourth to the fifth movement. Thus, there is more overlapping information arising from the consistent, neighbouring keypresses for the last index finger movement, compared to the first index finger movement of the next trial. A strong difference (larger neural representation distance) between these two movements is, therefore, not surprising, given the task design, and this difference is also expected to increase with learning, given the increase in tapping speed, and the consequent stronger overlap in representations for consecutive keypresses. Furthermore, initiating a new sequence involves pre-planning, while ongoing practice relies on online planning (Ariani et al., eNeuro 2021), i.e., two mental operations that are dissociable at the level of neural representation (Ariani et al., bioRxiv 2023).
The Reviewer argues that the comparison of last finger movement of a trial and the first in the next trial are performed in different circumstances and contexts. This is an important point and one we tend to agree with. For this task, the first sequence in a practice trial is pre-planned before the first keypress is performed. This occurs in a somewhat different context from the sequence iterations that follow, which involve temporally overlapping planning, execution and evaluation processes. The Reviewer is concerned about a difference in the temporal mixing effect issue raised above between the first and last keypresses performed in a trial. Please, note that since neural representations of individual actions are competitively queued during the pre-planning period in a manner that reflects the ordinal structure of the learned sequence (Kornysheva et al., 2019), mixing effects are most likely present also for the first keypress in a trial.
Separately, the Reviewer suggests that contextualization during early learning may reflect preplanning or online planning. This is an interesting proposal. Given the decoding time-window used in this investigation, we cannot dissect separate contributions of planning, memory and sensory feedback to contextualization. Taking advantage of the superior temporal resolution of MEG relative to fMRI tools, work under way in our lab is investigating decoding time-windows more appropriate to address each of these questions.
Given these differences in the physical context and associated mental processes, it is not surprising that "offline differentiation", as defined here, is more pronounced than "online differentiation". For the latter, the authors compared movements that were better matched regarding the presence of consistent preceding and subsequent keypresses (online differentiation was defined as the mean difference between all first vs. last index finger movements during practice). It is unclear why the authors did not follow a similar definition for "online differentiation" as for "micro-online gains" (and, indeed, a definition that is more consistent with their definition of "offline differentiation"), i.e., the difference between the first index finger movement of the first correct sequence during practice, and the last index finger of the last correct sequence. While these two movements are, again, not matched for the presence of neighbouring keypresses (see the argument above), this mismatch would at least be the same across "offline differentiation" and "online differentiation", so they would be more comparable.
This is the same point made earlier by Reviewer #2, and we agree with this assessment. As stated in the response to Reviewer #2 above, we have now carried out quantification of online contextualization using this approach and included it in the revised manuscript. We thank the Reviewer for this suggestion.
A further complication in interpreting the results regarding "contextualization" stems from the visual feedback that participants received during the task. Each keypress generated an asterisk shown above the string on the screen, irrespective of whether the keypress was correct or incorrect. As a result, incorrect (e.g., additional, or missing) keypresses could shift the phase of the visual feedback string (of asterisks) relative to the ordinal position of the current movement in the sequence (e.g., the fifth movement in the sequence could coincide with the presentation of any asterisk in the string, from the first to the fifth). Given that more incorrect keypresses are expected at the start of the experiment, compared to later stages, the consistency in visual feedback position, relative to the ordinal position of the movement in the sequence, increased across the experiment. A better differentiation between the first and the fifth movement with learning could, therefore, simply reflect better decoding of the more consistent visual feedback, based either on the feedback-induced brain response, or feedback-induced eye movements (the study did not include eye tracking). It is not clear why the authors introduced this complicated visual feedback in their task, besides consistency with their previous studies.
We strongly agree with the Reviewer that eye movements related to task engagement are important to rule out as a potential driver of the decoding accuracy or contextualizaton effect. We address this issue above in response to a question raised by Reviewer #1 about the impact of movement related artefacts on our findings.
First, the assumption the Reviewer makes here about the distribution of errors in this task is incorrect. On average across subjects, 2.32% ± 1.48% (mean ± SD) of all keypresses performed were errors, which were evenly distributed across the four possible keypress responses. While errors increased progressively over practice trials, they did so in proportion to the increase in correct keypresses, so that the overall ratio of correct-to-incorrect keypresses remained stable over the training session. Thus, the Reviewer’s assumptions that there is a higher relative frequency of errors in early trials, and a resulting systematic trend phase shift differences between the visual display updates (i.e. – a change in asterisk position above the displayed sequence) and the keypress performed is not substantiated by the data. To the contrary, the asterisk position on the display and the keypress being executed remained highly correlated over the entire training session. We now include a statement about the frequency and distribution of errors in the revised manuscript.
Given this high correlation, we firmly agree with the Reviewer that the issue of eye movement related artefacts is still an important one to address. Fortunately, we did collect eye movement data during the MEG recordings so were able to investigate this. As detailed in the response to Reviewer #1 above, we found that gaze positions and eye-movement velocity time-locked to visual display updates (i.e. – a change in asterisk position above the displayed sequence) did not reflect the asterisk location above chance levels (Overall cross-validated accuracy = 0.21817; see Author response image 1). Furthermore, an inspection of the eye position data revealed that most participants on most trials displayed random walk gaze patterns around a center fixation point, indicating that participants did not attend to the asterisk position on the display. This is consistent with intrinsic generation of the action sequence, and congruent with the fact that the display does not provide explicit feedback related to performance. As pointed out above, a similar real-world example would be manually inputting a long password into a secure online application. In this case, one intrinsically generates the sequence from memory and receives similar feedback about the password sequence position (also provided as asterisks), which is typically ignored by the user.
The minimal participant engagement with the visual display in this explicit sequence learning motor task (which is highly generative in nature) contrasts markedly with behavior observed when reactive responses to stimulus cues are needed in the serial reaction time task (SRTT). This is a crucial difference that must be carefully considered when comparing findings across studies using the two sequence learning tasks.
The authors report a significant correlation between "offline differentiation" and cumulative microoffline gains. However, it would be more informative to correlate trial-by-trial changes in each of the two variables. This would address the question of whether there is a trial-by-trial relation between the degree of "contextualization" and the amount of micro-offline gains - are performance changes (micro-offline gains) less pronounced across rest periods for which the change in "contextualization" is relatively low? Furthermore, is the relationship between micro-offline gains and "offline differentiation" significantly stronger than the relationship between micro-offline gains and "online differentiation"?
In response to a similar issue raised above by Reviewer #2, we now include new analyses comparing correlation magnitudes between (1) “online differentiation” vs micro-online gains, (2) “online differentiation” vs micro-offline gains and (3) “offline differentiation” and micro-offline gains (see Figure 5 – figure supplement 4, 5 and 6). These new analyses and results have been added to the revised manuscript. Once again, we thank both Reviewers for this suggestion.
The authors follow the assumption that micro-offline gains reflect offline learning.
We disagree with this statement. The original (Bonstrup et al., 2019) paper clearly states that micro-offline gains do not necessarily reflect offline learning in some cases and must be carefully interpreted based upon the behavioral context within which they are observed. Further, the paper lays out the conditions under which one can have confidence that micro-offline gains reflect offline learning. In fact, the excellent meta-analysis of (Pan & Rickard, 2015), which re-interprets the benefits of sleep in overnight skill consolidation from a “reactive inhibition” perspective, was a crucial resource in the experimental design of our initial study (Bonstrup et al., 2019), as well as in all our subsequent work. Pan & Rickard state:
“Empirically, reactive inhibition refers to performance worsening that can accumulate during a period of continuous training (Hull, 1943 . It tends to dissipate, at least in part, when brief breaks are inserted between blocks of training. If there are multiple performance-break cycles over a training session, as in the motor sequence literature, performance can exhibit a scalloped effect, worsening during each uninterrupted performance block but improving across blocks(Brawn et al., 2010; Rickard et al., 2008 . Rickard, Cai, Rieth, Jones, and Ard (2008 and Brawn, Fenn, Nusbaum, and Margoliash (2010 (Brawn et al., 2010; Rickard et al., 2008 demonstrated highly robust scalloped reactive inhibition effects using the commonly employed 30 s–30 s performance break cycle, as shown for Rickard et al.’s (2008 massed practice sleep group in Figure 2. The scalloped effect is evident for that group after the first few 30 s blocks of each session. The absence of the scalloped effect during the first few blocks of training in the massed group suggests that rapid learning during that period masks any reactive inhibition effect.”
Crucially, Pan & Rickard make several concrete recommendations for reducing the impact of the reactive inhibition confound on offline learning studies. One of these recommendations was to reduce practice times to 10s (most prior sequence learning studies up until that point had employed 30s long practice trials). They state:
“The traditional design involving 30 s-30 s performance break cycles should be abandoned given the evidence that it results in a reactive inhibition confound, and alternative designs with reduced performance duration per block used instead (Pan & Rickard, 2015 . One promising possibility is to switch to 10 s performance durations for each performance-break cycle Instead (Pan & Rickard, 2015 . That design appears sufficient to eliminate at least the majority of the reactive inhibition effect (Brawn et al., 2010; Rickard et al., 2008 .”
We mindfully incorporated recommendations from (Pan & Rickard, 2015) into our own study designs including 1) utilizing 10s practice trials and 2) constraining our analysis of micro-offline gains to early learning trials (where performance monotonically increases and 95% of overall performance gains occur), which are prior to the emergence of the “scalloped” performance dynamics that are strongly linked to reactive inhibition effects.
However, there is no direct evidence in the literature that micro-offline gains really result from offline learning, i.e., an improvement in skill level.
We strongly disagree with the Reviewer’s assertion that “there is no direct evidence in the literature that micro-offline gains really result from offline learning, i.e., an improvement in skill level.” The initial (Bonstrup et al., 2019) report was followed up by a large online crowd-sourcing study (Bonstrup et al., 2020). This second (and much larger) study provided several additional important findings supporting our interpretation of micro-offline gains in cases where the important behavioral conditions clarified above were met (see Author response image 4 below for further details on these conditions).
Author response image 4.
This Figure shows that micro-offline gains o ser ed in learning and nonlearning contexts are attri uted to different underl ing causes. Micro-offline and online changes relative to overall trial-by-trial learning. This figure is based on data from (Bonstrup et al., 2019). During early learning, micro-offline gains (red bars) closely track trial-by-trial performance gains (green line with open circle markers), with minimal contribution from micro-online gains (blue bars). The stated conclusion in Bönstrup et al. (2019) is that micro-offline gains only during this Early Learning stage reflect rapid memory consolidation (see also (Bonstrup et al., 2020)). After early learning, about practice trial 11, skill plateaus. This plateau skill period is characterized by a striking emergence of coupled (and relatively stable) micro-online drops and micro-offline increases. Bönstrup et al. (2019) as well as others in the literature (Brooks et al., 2024; Gupta & Rickard, 2022; Florencia Jacobacci et al., 2020), argue that micro-offline gains during the plateau period likely reflect recovery from inhibitory performance factors such as reactive inhibition or fatigue, and thus must be excluded from analyses relating micro-offline gains to skill learning. The Non-repeating groups in Experiments 3 and 4 from Das et al. (2024) suffer from a lack of consideration of these known confounds (end of Fig legend).
Evidence documented in that paper (Bonstrup et al., 2020) showed that micro-offline gains during early skill learning were: 1) replicable and generalized to subjects learning the task in their daily living environment (n=389); 2) equivalent when significantly shortening practice period duration, thus confirming that they are not a result of recovery from performance fatigue (n=118); 3) reduced (along with learning rates) by retroactive interference applied immediately after each practice period relative to interference applied after passage of time (n=373), indicating stabilization of the motor memory at a microscale of several seconds consistent with rapid consolidation; and 4) not modified by random termination of the practice periods, ruling out a contribution of predictive motor slowing (N = 71) (Bonstrup et al., 2020). Altogether, our findings were strongly consistent with the interpretation that micro-offline gains reflect memory consolidation supporting early skill learning. This is precisely the portion of the learning curve (Pan & Rickard, 2015) refer to when they state “…rapid learning during that period masks any reactive inhibition effect”.
This interpretation is further supported by brain imaging evidence linking known memory-related networks and consolidation mechanisms to micro-offline gains. First, we reported that the density of fast hippocampo-neocortical skill memory replay events increases approximately three-fold during early learning inter-practice rest periods with the density explaining differences in the magnitude of micro-offline gains across subjects (Buch et al., 2021). Second, Jacobacci et al. (2020) independently reproduced our original behavioral findings and reported BOLD fMRI changes in the hippocampus and precuneus (regions also identified in our MEG study (Buch et al., 2021)) linked to micro-offline gains during early skill learning. These functional changes were coupled with rapid alterations in brain microstructure in the order of minutes, suggesting that the same network that operates during rest periods of early learning undergoes structural plasticity over several minutes following practice (Deleglise et al., 2023). Crucial to this point, Chen et al. (2024) and Sjøgård et al (2024) provided direct evidence from intracranial EEG in humans linking sharp-wave ripple density during rest periods (which are known markers for neural replay (Buzsaki, 2015)) in the human hippocampus (80-120 Hz) to micro-offline gains during early skill learning.
Thus, there is now substantial converging evidence in humans across different indirect noninvasive and direct invasive recording techniques linking hippocampal activity, neural replay dynamics and offline performance gains in skill learning.
On the contrary, recent evidence questions this interpretation (Gupta & Rickard, npj Sci Learn 2022; Gupta & Rickard, Sci Rep 2024; Das et al., bioRxiv 2024). Instead, there is evidence that micro-offline gains are transient performance benefits that emerge when participants train with breaks, compared to participants who train without breaks, however, these benefits vanish within seconds after training if both groups of participants perform under comparable conditions (Das et al., bioRxiv 2024).
The recent work of (Gupta & Rickard, 2022, 2024) does not present any data that directly opposes our finding that early skill learning (Bonstrup et al., 2019) is expressed as micro-offline gains during rest breaks. These studies are an extension of the Rickard et al (2008) paper that employed a massed (30s practice followed by 30s breaks) vs spaced (10s practice followed by 10s breaks) experimental design to assess if recovery from reactive inhibition effects could account for performance gains measured after several minutes or hours. Gupta & Rickard (2022) added two additional groups (30s practice/10s break and 10s practice/10s break as used in the work from our group). The primary aim of the study was to assess whether it was more likely that changes in performance when retested 5 minutes after skill training (consisting of 12 practice trials for the massed groups and 36 practice trials for the spaced groups) had ended reflected memory consolidation effects or recovery from reactive inhibition effects. The Gupta & Rickard (2024) follow-up paper employed a similar design with the primary difference being that participants performed a fixed number of sequences on each trial as opposed to trials lasting a fixed duration. This was done to facilitate the fitting of a quantitative statistical model to the data.
To reiterate, neither study included any analysis of micro-online or micro-offline gains and did not include any comparison focused on skill gains during early learning trials (only at retest 5 min later). Instead, Gupta & Rickard (2022), reported evidence for reactive inhibition effects for all groups over much longer training periods than early learning. In fact, we reported the same findings for trials following the early learning period in our original 2019 paper (Bonstrup et al., 2019) (Author response image 4). Please, note that we also reported that cumulative microoffline gains over early learning did not correlate with overnight offline consolidation measured 24 hours later (Bonstrup et al., 2019) (see the Results section and further elaboration in the Discussion). We interpreted these findings as indicative that the mechanisms underlying offline gains over the micro-scale of seconds during early skill learning versus over minutes or hours very likely differ.
In the recent preprint from (Das et al., 2024), the authors make the strong claim that “micro-offline gains during early learning do not reflect offline learning” which is not supported by their own data. The authors hypothesize that if “micro-offline gains represent offline learning, participants should reach higher skill levels when training with breaks, compared to training without breaks”. The study utilizes a spaced vs. massed practice groups between-subjects design inspired by the reactive inhibition work from Rickard and others to test this hypothesis.
Crucially, their design incorporates only a small fraction of the training used in other investigations to evaluate early skill learning (Bonstrup et al., 2020; Bonstrup et al., 2019; Brooks et al., 2024; Buch et al., 2021; Deleglise et al., 2023; F. Jacobacci et al., 2020; Mylonas et al., 2024). A direct comparison between the practice schedule designs for the spaced and massed groups in Das et al., and the training schedule all participants experienced in the original Bönstrup et al. (2019) paper highlights this issue as well as several others (Author response image 5):
Author response image 5.
This figure shows (A) Comparison of Das et al. Spaced & Massed group training session designs, and the training session design from the original (Bonstrup et al., 2019) paper. Similar to the approach taken by Das et al., all practice is visualized as 10-second practice trials with a variable number (either 0, 1 or 30) of 10-second-long inter-practice rest intervals to allow for direct comparisons between designs. The two key takeaways from this comparison are that (1) the intervention differences (i.e. – practice schedules) between the Massed and Spaced groups from the Das et al. report are extremely small (less than 12% of the overall session schedule) (gaps in the red shaded area) and (2) the overall amount of practice is much less than compared to the design from the original Bönstrup report (Bonstrup et al., 2019) (which has been utilized in several subsequent studies). (B) Group-level learning curve data from Bönstrup et al. (2019) (Bonstrup et al., 2019) is used to estimate the performance range accounted for by the equivalent periods covering Test 1, Training 1 and Test 2 from Das et al (2024). Note that the intervention in the Das et al. study is limited to a period covering less than 50% of the overall learning range (end of figure legend).
Participants in the original (Bonstrup et al., 2019) experienced 157.14% more practice time and 46.97% less inter-practice rest time than the Spaced group in the Das et al. study (Author response image 5). Thus, the overall amount of practice and rest differ substantially between studies, with much more limited training occurring for participants in Das et al.
In addition, the training interventions (i.e. – the practice schedule differences between the Spaced and Massed groups) were designed in a manner that minimized any chance of effectively testing their hypothesis. First, the interventions were applied over an extremely short period relative to the length of the total training session (5% and 12% of the total training session for Massed and Spaced groups, respectively; see gaps in the red shaded area in Author response image 5). Second, the intervention was applied during a period in which only half of the known total learning occurs. Specifically, we know from Bönstrup et al. (2019) that only 46.57% of the total performance gains occur in the practice interval covered by Das et al Training 1 intervention. Thus, early skill learning as evaluated by multiple groups (Bonstrup et al., 2020; Bonstrup et al., 2019; Brooks et al., 2024; Buch et al., 2021; Deleglise et al., 2023; F. Jacobacci et al., 2020; Mylonas et al., 2024), is in the Das et al experiment amputated to about half.
Furthermore, a substantial amount of learning takes place during Das et al’s Test 1 and Test 2 periods (32.49% of total gains combined). The fact that substantial learning is known to occur over both the Test 1 (18.06%) and Test 2 (14.43%) intervals presents a fundamental problem described by Pan and Rickard (Pan & Rickard, 2015). They reported that averaging over intervals where substantial performance gains occur (i.e. – performance is not stable) inject crucial artefacts into analyses of skill learning:
“A large amount of averaging has the advantage of yielding more precise estimates of each subject’s pretest and posttest scores and hence more statistical power to detect a performance gain. However, calculation of gain scores using that strategy runs the risk that learning that occurs during the pretest and (or posttest periods (i.e., online learning is incorporated into the gain score (Rickard et al., 2008; Robertson et al., 2004 .”
The above statement indicates that the Test 1 and Test 2 performance scores from Das et al. (2024) are substantially contaminated by the learning rate within these intervals. This is particularly problematic if the intervention design results in different Test 2 learning rates between the two groups. This in fact, is apparent in their data (Figure 1C,E of the Das et al., 2024 preprint) as the Test 2 learning rate for the Spaced group is negative (indicating a unique interference effect observable only for this group). Specifically, the Massed group continues to show an increase in performance during Test 2 and 4 relative to the last 10 seconds of practice during Training 1 and 2, respectively, while the Spaced group displays a marked decrease. This post-training performance decrease for the Spaced group is in stark contrast to the monotonic performance increases observed for both groups at all other time-points. One possible cause could be related to the structure of the Test intervals, which include 20 seconds of uninterrupted practice. For the Spaced group, this effectively is a switch to a Massed practice environment (i.e., two 10-secondlong practice trials merged into one long trial), which interferes with greater Training 1 interval gains observed for the Space group. Interestingly, when statistical comparisons between the groups are made at the time-points when the intervention is present (Figure 1E) then the stated hypothesis, “If micro-offline gains represent offline learning, participants should reach higher skill levels when training with breaks, compared to training without breaks”, is confirmed.
In summary, the experimental design and analyses used by Das et al does not contradict the view that early skill learning is expressed as micro-offline gains during rest breaks. The data presented by Gupta and Rickard (2022, 2024) and Das et al. (2024) is in many ways more confirmatory of the constraints employed by our group and others with respect to experimental design, analysis and interpretation of study findings, rather than contradictory. Still, it does highlight a limitation of the current micro-online/offline framework, which was originally only intended to be applied to early skill learning over spaced practice schedules when reactive inhibition effects are minimized (Bonstrup et al., 2019; Pan & Rickard, 2015). Extrapolation of this current framework to postplateau performance periods, longer timespans, or non-learning situations (e.g. – the Nonrepeating groups from Das et al. (2024)), when reactive inhibition plays a more substantive role, is not warranted. Ultimately, it will be important to develop new paradigms allowing one to independently estimate the different coincident or antagonistic features (e.g. - memory consolidation, planning, working memory and reactive inhibition) contributing to micro-online and micro-offline gains during and after early skill learning within a unifying framework.
Recommendations for the authors:
Reviewer #1 (Recommendations for the authors):
(1) I found Figure 2B too small to be useful, as the actual elements of the cells are very hard to read.
We have removed the grid colormap panel (top-right) from Figure 2B. All of this colormap data is actually a subset of data presented in Figure 2 – figure supplement 1, so can still be found there.
Reviewer #2 (Recommendations for the authors):
(1) Related to the first point in my concerns, I would suggest the authors compare decoding accuracy between correct presses followed by correct vs. incorrect presses. This would clarify if the decoder is actually taking the MEG signal for subsequent press into account. I would also suggest the authors use pre-movement MEG features and post-movement features with shorter windows and compare each result with the results for the original post-movement MEG feature with a longer window.
The present study does not contain enough errors to perform the analysis proposed by the Reviewer. As noted above, we did re-examine our data and now report a new control regression analysis, all of which indicate that the proximity between keypresses does not explain contextualization effects.
(2) I was several times confused by the author's use of "neural representation of an action" or "sequence action representations" in understanding whether these terms refer to representation on the level of whole-brain, region (as defined by the specific parcellation used), or voxels. In fact, what is submitted to the decoder is some complicated whole-brain MEG feature (i.e., the "neural representation"), which is a hybrid of voxel and parcel features that is further dimension-reduced and not immediately interpretable. Clarifying this point early in the text and possibly using some more sensible terms, such as adding "brain-wise" before the "sequence action representation", would be the most helpful for the readers.
We now clarified this terminology in the revised manuscript.
(3) Although comparing many different ways in feature selection/reduction, time window selection, and decoder types is undoubtedly a meticulous work, the current version of the manuscript seems still lacking some explanation about the details of these methodological choices, like which decoding method was actually used to report the accuracy, whether or not different decoding methods were chosen for individual participants' data, how training data was selected (is it all of the correct presses in Day 1 data?), whether the frequency power or signal amplitude was used, and so on. I would highly appreciate these additional details in the Methods section.
The reported accuracies were based on linear discriminant analysis classifier. A comparison of different decoders (Figure 3 – figure supplement 4) shows LDA was the optimal choice.
Whether or not different decoding methods were chosen for individual participants' data
We selected the same decoder (LDA) performance to report the final accuracy.
How training data was selected (is it all of the correct presses in Day 1 data?),
Decoder training was conducted as a randomized split of the data (all correct keypresses of Day 1) into training (90%) and test (10%) samples for 8 iterations.
Whether the frequency power or signal amplitude was used
Signal amplitude was used for feature calculation.
(4) In terms of the Methods, please consider adding some references about the 'F1 score', the 'feature importance score,' and the 'MRMR-based feature ranking,' as the main readers of the current paper would not be from the machine learning community. Also, why did the LDA dimensionality reduction reduce accuracy specifically for the voxel feature?
We have now added the following statements to the Methods section that provide more detailed descriptions and references for these metrics:
“The F1 score, defined as the harmonic mean of the precision (percentage of true predictions that are actually true positive) and recall (percentage of true positives that were correctly predicted as true) scores, was used as a comprehensive metric for all one-versus-all keypress state decoders to assess class-wise performance that accounts for both false-positive and false-negative prediction tendencies [REF]. A weighted mean F1 score was then computed across all classes to assess the overall prediction performance of the multi-class model.”
and
“Feature Importance Scores
The relative contribution of source-space voxels and parcels to decoding performance (i.e. – feature importance score) was calculated using minimum redundant maximum relevance (MRMR) and highlighted in topography plots. MRMR, an approach that combines both relevance and redundancy metrics, ranked individual features based upon their significance to the target variable (i.e. – keypress state identity) prediction accuracy and their non-redundancy with other features.”
As stated in the Reviewer responses above, the dimensionality of the voxel-space feature set is very high (i.e. – 15684). LDA attempts to map the input features onto a much smaller dimensional space (number of classes-1; e.g. – 3 dimensions for 4-class keypress decoding). It is likely that the reduction in accuracy observed only for the voxel-space feature was due to the loss of relevant information during the mapping process that resulted in reduced accuracy. This reduction in accuracy for voxel-space decoding was specific to LDA. Figure 3—figure supplement 3 shows that voxel-space decoder performance actually improved when utilizing alternative dimensionality reduction techniques.
(5) Paragraph 9, lines #139-142: "Notably, decoding associated with index finger keypresses (executed at two different ordinal positions in the sequence) exhibited the highest number of misclassifications of all digits (N = 141 or 47.5% of all decoding errors; Figure 3C), raising the hypothesis that the same action could be differentially represented when executed at different learning state or sequence context locations."
This does not seem to be a fair comparison, as the index finger appears twice as many as the other fingers do in the sequence. To claim this, proper statistical analysis needs to be done taking this difference into account.
We thank the Reviewer for bringing this issue to our attention. We have now corrected this comparison to evaluate relative false negative and false positive rates between individual keypress state decoders, and have revised this statement in the manuscript as follows:
“Notably, decoding of index finger keypresses (executed at two different ordinal positions in the sequence) exhibited the highest false negative (0.116 per keypress) and false positive (0.043 per keypress) misclassification rates compared with all other digits (false negative rate range = [0.067 0.114]; false positive rate range = [0.020 0.037]; Figure 3C), raising the hypothesis that the same action could be differentially represented when executed within different contexts (i.e. - different learning states or sequence locations).”
(6) Finally, the authors could consider acknowledging in the Discussion that the contribution of micro-offline learning to genuine skill learning is still under debate (e.g., Gupta and Rickard, 2023; 2024; Das et al., bioRxiv, 2024).
We have added a paragraph in the Discussion that addresses this point.
Reviewer #3 (Recommendations for the authors):
In addition to the additional analyses suggested in the public review, I have the following suggestions/questions:
(1) Given that the authors introduce a new decoding approach, it would be very helpful for readers to see a distribution of window sizes and window onsets eventually used across individuals, at least for the optimized decoder.
We have now included a new supplemental figure (Figure 4 – figure Supplement 2) that provides this information.
(2) Please explain in detail how you arrived at the (interpolated?) group-level plot shown in Figure 1B, starting from the discrete single-trial keypress transition times. Also, please specify what the shading shows.
Instantaneous correct sequence speed (skill measure) was quantified as the inverse of time (in seconds) required to complete a single iteration of a correctly generated full 5-item sequence. Individual keypress responses were labeled as members of correct sequences if they occurred within a 5-item response pattern matching any possible circular shifts of the 5-item sequence displayed on the monitor (41324). This approach allowed us to quantify a measure of skill within each practice trial at the resolution of individual keypresses. The dark line indicates the group mean performance dynamics for each trial. The shaded region indicates the 95% confidence limit of the mean (see Methods).
(3) Similarly, please explain how you arrived at the group-level plot shown in Figure 1C. What are the different colored lines (rows) within each trial? How exactly did the authors reach the conclusion that KTT variability stabilizes by trial 6?
Figure 1C provides additional information to the correct sequence speed measure above, as it also tracks individual transition speed composition over learning. Figure 1C, thus, represents both changes in overall correct sequence speed dynamics (indicated by the overall narrowing of the horizontal speed lines moving from top to bottom) and the underlying composition of the individual transition patterns within and across trials. The coloring of the lines is a shading convention used to discriminate between different keypress transitions. These curves were sampled with 1ms resolution, as in Figure 1B. Addressing the underlying keypress transition patterns requires within-subject normalization before averaging across subjects. The distribution of KTTs was normalized to the median correct sequence time for each participant and centered on the mid-point for each full sequence iteration during early learning.
(4) Maybe I missed it, but it was not clear to me which of the tested classifiers was eventually used. Or was that individualized as well? More generally, a comparison of the different classifiers would be helpful, similar to the comparison of dimension reduction techniques.
We have now included a new supplemental figure that provides this information.
(5) Please add df and effect sizes to all statistics.
Done.
(6) Please explain in more detail your power calculation.
The study was powered to determine the minimum sample size needed to detect a significant change in skill performance following training using a one-sample t-test (two-sided; alpha = 0.05; 95% statistical power; Cohen’s D effect size = 0.8115 calculated from previously acquired data in our lab). The calculated minimum sample size was 22. The included study sample size (n = 27) exceeded this minimum.
This information is now included in the revised manuscript.
(7) The cut-off for the high-pass filter is unusually high and seems risky in terms of potential signal distortions (de Cheveigne, Neuron 2019). Why did the authors choose such a high cut-off?
The 1Hz high-pass cut-off frequency for the 1-150Hz band-pass filter applied to the continuous raw MEG data during preprocessing has been used in multiple previous MEG publications (Barratt et al., 2018; Brookes et al., 2012; Higgins et al., 2021; Seedat et al., 2020; Vidaurre et al., 2018).
(8) "Furthermore, the magnitude of offline contextualization predicted skill gains while online contextualization did not", lines 336/337 - where is that analysis?
Additional details pertaining to this analysis are now provided in the Results section (Figure 5 – figure supplement 4).
(9) How were feature importance scores computed?
We have now added a new subheading in the Methods section with a more detailed description of how feature importance scores were computed.
(10) Please add x and y ticks plus tick labels to Figure 5 - Figure Supplement 3, panel A
Done
(11) Line 369, what does "comparable" mean in this context?
The sentence in the “Study Participants” part of the Methods section referred to here has now been revised for clarity.
(12) In lines 496/497, please specify what t=0 means (KeyDown event, I guess?).
Yes, the KeyDown event occurs at t = 0. This has now been clarified in the revised manuscript.
(13) Please specify consistent boundaries between alpha- and beta-bands (they are currently not consistent in the Results vs. Methods (14/15 Hz or 15/16 Hz)).
We thank the Reviewer for alerting us to this discrepancy caused by a typographic error in the Methods. We have now corrected this so that the alpha (8-14 Hz) and beta-band (15-24 Hz) frequency limits are described consistently throughout the revised manuscript.
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Author response:
The following is the authors’ response to the original reviews.
Public Reviews:
Reviewer #1 (Public Review):
Summary:
In this manuscript, the authors present a novel CRISPR/Cas9-based genetic tool for the dopamine receptor dop1R2. Based on the known function of the receptor in learning and memory, they tested the efficacy of the genetic tool by knocking out the receptor specifically in mushroom body neurons. The data suggest that dop1R2 is necessary for longer-lasting memories through its action on ⍺/ß and ⍺'/ß' neurons but is dispensable for short-term memory and thus in ɣ neurons. The experiments impressively demonstrate the value of such a genetic tool and illustrate the specific function of the receptor in subpopulations of KCs for longer-term memories. The data presented in this manuscript are significant.
Reviewer #2 (Public Review):
Summary:
This manuscript examines the role of the dopamine receptor, Dop1R2, in memory formation. This receptor has complex roles in supporting different stages of memory, and the neural mechanisms for these functions are poorly understood. The authors are able to localize Dop1R2 function to the vertical lobes of the mushroom body, revealing a role in later (presumably middle-term) aversive and appetitive memory. In general, the experimental design is rigorous, and statistics are appropriately applied. While the manuscript provides a useful tool, it would be strengthened further by additional mechanistic studies that build on the rich literature examining the roles of dopamine signaling in memory formation. The claim that Dop1R2 is involved in memory formation is strongly supported by the data presented, and this manuscript adds to a growing literature revealing that dopamine is a critical regulator of olfactory memory. However, the manuscript does not necessarily extend much beyond our understanding of Dop1R2 in memory formation, and future work will be needed to fully characterize this reagent and define the role of Dop1R2 in memory.
Strengths:
(1) The FRT lines generated provide a novel tool for temporal and spatially precise manipulation of Dop1R2 function. This tool will be valuable to study the role of Dop1R2 in memory and other behaviors potentially regulated by this gene.
(2) Given the highly conserved role of Dop1R2 in memory and other processes, these findings have a high potential to translate to vertebrate species.
Weaknesses:
(1) The authors state Dop1R2 associates with two different G-proteins. It would be useful to know which one is mediating the loss of aversive and appetitive memory in Dop1R2 knockout flies.
We thank you for the insightful comment. We agree that it would be very useful to know which G-proteins are transmitting Dop1R2 signaling. To that extent, we examined single-cell transcriptomics data to check the level of co-expression of Dop1R2 with G-proteins that are of interest to us. (Figure 1 S1)
Lines 312-325
“Some RNA binding proteins and Immediate early genes help maintain identities of Mushroom body cells and are regulators of local transcription and translation (de Queiroz et al., 2025; Raun et al., 2025). So, the availability of different G-proteins may change in different lobes and during different phases of memory. The G-protein via which GPCRs signal, may depend on the pool of available G-proteins in the cell/sub-cellular region (Hermans, 2003)., Therefore, Dop1R2 may signal via different G-proteins in different compartments of the Mushroom body and also different compartments of the neuron. We looked at Gαo and Gαq as they are known to have roles in learning and forgetting (Ferris et al., 2006; Himmelreich et al., 2017). We found that Dop1R2 co-expresses more frequently with Gαo than with Gαq (Figure 1 S1). While there is evidence for Dop1R2 to act via Gαq (Himmelreich et al., 2017). It is difficult to determine whether this interaction is exclusive, or if Dop1R2 can also be coupled to other G-proteins. It will be interesting to determine the breadth of G-proteins that are involved in Dop1R2 signaling.”
(2) It would be interesting to examine 24hr aversive memory, in addition to 24hr appetitive memory.
This is indeed an important point and we agree that it will complete the assessment of temporally distinct memory traces. We therefore performed the Aversive LTM experiments and include them in the results.
Lines 208-228
“24h memory is impaired by loss of Dop1R2
Next, we wanted to see if later memory forms are also affected. One cycle of reward training is sufficient to create LTM (Krashes & Waddell, 2008), while for aversive memory, 5-6 cycles of electroshock-trainings are required to obtain robust long-term memory scores (Tully et al., 1994). So, we looked at both, 24h aversive and appetitive memory. For aversive LTM, the flies were tested on the Y-Maze apparatus as described in (Mohandasan et al., (2022).
Flipping out Dop1R2 in the whole MB causes a reduced 24h memory performance (Figure 4A, E). No phenotype was observed when Ddop1R2 was flipped out in the γ-lobe (Figure 4B, F). However, similar to 2h memory, loss of Ddop1R2 in the α/β-lobes (Figure 4C, G) or the α’/β’-lobes (Figure 4D, H) causes a reduction in memory performance. Thus, Dop1R2 seems to be involved in aversive and appetitive LTM in the α/β-lobes and the α’/β’-lobes.
Previous studies have shown mutation in the Dop1R2 receptor leads to improvement in LTM when a single shock training paradigm is used (Berry et al., 2012). As we found that it disrupts LTM, we wanted to verify if the absence of Dop1R2 outside the MB is what leads to an improvement in memory. To that extent, we tested panneuronal flip-out of Dop1R2 flies for 6hr and 24hr memory upon single shock using the elav-Gal4 driver. We found that it did not improve memory at both time points (Figure 4 S1). Confirming that flipping out Dop1R2 panneuronally does not improve LTM (Figure 4 S1C) and highlighting its irrelevance in memory outside the MB.”
(3) The manuscript would be strengthened by added functional analysis. What are the DANs that signal through Dop1R. How do these knockouts impact MBONs?
We thank you for this question. We indeed agree that it is a highly relevand and open question, how distinct DANs signal via distinct Dopamine receptors. Our work here uniquely focusses on Dop1R2 within the MB. We aim to investigate other DopRs and the connection between DANs in the future using similar approaches.
(4) Also in Figure 2, the lobe-specific knockouts might be moved to supplemental since there is no effect. Instead, consider moving the control sensory tests into the main figure.
We thank you for this suggestion and understand that in Figure 2 no significant difference is seen. However, we have emphasized in the text that the results from the supplementary figures are just to confirm that the modifications made at the Dop1R2 locus did not alter its normal function.
Lines 156-162
“We wanted to see if flipping out Dop1R2 in the MB affects memory acquisition and STM by using classical olfactory conditioning. In short, a group of flies is presented with an odor coupled to an electric shock (aversive) or sugar (appetitive) followed by a second odor without stimulus. For assessing their memory, flies can freely choose between the odors either directly after training (STM) or at a later timepoint.
To ensure that the introduced genetic changes to the Dop1R2 locus do not interfere with behavior we first checked the sensory responses of that line”
(5) Can the single-cell atlas data be used to narrow down the cell types in the vertical lobes that express Dop1R2? Is it all or just a subset?
This is indeed an interesting question, and we thank you for mentioning it. To address this as best as we could, we analyzed the single cell transcriptomic data from (Davie et al., 2018) and presented it in Figure 1 S1.
Reviewer #3 (Public Review):
Summary:
Kaldun et al. investigated the role of Dopamine Receptor Dop1R2 in different types and stages of olfactory associative memory in Drosophila melanogaster. Dop1R2 is a type 1 Dopamine receptor that can act both through Gs-cAMP and Gq-ERCa2+ pathways. The authors first developed a very useful tool, where tissue-specific knock-out mutants can be generated, using Crispr/Cas9 technology in combination with the powerful Gal4/UAS gene-expression toolkit, very common in fruit flies.
They direct the K.O. mutation to intrinsic neurons of the main associative memory centre fly brain-the mushroom body (MB). There are three main types of MB-neurons, or Kenyon cells, according to their axonal projections: a/b; a'/b', and g neurons.
Kaldun et al. found that flies lacking dop1R2 all over the MB displayed impaired appetitive middle-term (2h) and long-term (24h) memory, whereas appetitive short-term memory remained intact. Knocking-out dop1R2 in the three MB neuron subtypes also impaired middle-term, but not short-term, aversive memory.
These memory defects were recapitulated when the loss of the dop1R2 gene was restricted to either a/b or a'/b', but not when the loss of the gene was restricted to g neurons, showcasing a compartmentalized role of Dop1R2 in specific neuronal subtypes of the main memory centre of the fly brain for the expression of middle and long-term memories.
Strengths:
(1) The conclusions of this paper are very well supported by the data, and the authors systematically addressed the requirement of a very interesting type of dopamine receptor in both appetitive and aversive memories. These findings are important for the fields of learning and memory and dopaminergic neuromodulation among others. The evidence in the literature so far was generated in different labs, each using different tools (mutants, RNAi knockdowns driven in different developmental stages...), different time points (short, middle, and long-term memory), different types of memories (Anesthesia resistant, which is a type of protein synthesis independent consolidated memory; anesthesia sensitive, which is a type of protein synthesis-dependent consolidated memory; aversive memory; appetitive memory...) and different behavioral paradigms. A study like this one allows for direct comparison of the results, and generalized observations.
(2) Additionally, Kaldun and collaborators addressed the requirement of different types of Kenyon cells, that have been classically involved in different memory stages: g KCs for memory acquisition and a/b or a'/b' for later memory phases. This systematical approach has not been performed before.
(3) Importantly, the authors of this paper produced a tool to generate tissue-specific knock-out mutants of dop1R2. Although this is not the first time that the requirement of this gene in different memory phases has been studied, the tools used here represent the most sophisticated genetic approach to induce a loss of function phenotypes exclusively in MB neurons.
Weaknesses:
(1) Although the paper does have important strengths, the main weakness of this work is that the advancement in the field could be considered incremental: the main findings of the manuscript had been reported before by several groups, using tissue-specific conditional knockdowns through interference RNAi. The requirement of Dop1R2 in MB for middle-term and long-term memories has been shown both for appetitive (Musso et al 2015, Sun et al 2020) and aversive associations (Plaçais et al 2017).
Thank you for this comment. We believe that the main takeaway from the paper is the elegant tool we developed, to study the role of Dop1R2 in fruit flies by effectively flipping it out spatio-temporally. Additionally, we studied its role in all types of olfactory associative memory to establish it as a robust tool that can be used for further research in place of RNAi knockouts which are shown to be less efficient in insects as mentioned in the texts in line 394-398.
“The genetic tool we generated here to study the role of the Dop1R2 dopamine receptor in cells of interest, is not only a good substitute for RNAi knockouts, which are known to be less efficient in insects (Joga et al., 2016), but also provides versatile possibilities as it can be used in combination with the powerful genetic tools of Drosophila.”
(2) The approach used here to genetically modify memory neurons is not temporally restricted. Considering the role of dopamine in the correct development of the nervous system, one must consider the possible effects that this manipulation can have in the establishment of memory circuits. However, previous studies addressing this question restricted the manipulation of Dop1R2 expression to adulthood, leading to the same findings than the ones reported in this paper for both aversive and appetitive memories, which solidifies the findings of this paper.
We thank you for this comment and we agree that it would be important to show a temporally restricted effect of Dop1R2 knockout. To assess this and rule out potential developmental defects we decided to restrict the knockout to the post-eclosion stage and to include these results.
Lines 230-250
“Developmental defects are ruled out in a temporally restricted Dop1R2 conditional knockout.
To exclude developmental defects in the MB caused by flip-out of Dop1R2, we stained fly brains with a FasII antibody. Compared to genetic controls, flies lacking Dop1R2 in the mushroom body had unaltered lobes (Figure 4 S2C).
Regardless, we wanted to control for developmental defects leading to memory loss in flip-out flies. So, we generated a Gal80ts-containing line, enabling the temporal control of Dop1R2 knockout in the entire mushroom body (MB). Given that the half-life of the receptor remains unknown, we assessed both aversive short-term memory (STM) and long-term memory (LTM) to determine whether post-eclosion ablation of Dop1R2 in the MB produced differences compared to our previously tested line, in which Dop1R2 was constitutively knocked out from fertilization. To achieve this, flies were maintained at 18°C until eclosion and subsequently shifted to 30°C for five to seven days. On the fifth day, training was conducted, followed by memory testing. Our results indicate that aversive STM was not significantly impaired in Dop1R2-deficient MBs compared to control flies (Figure 4 S3), consistent with our previous findings (Figure 2). However, aversive LTM was significantly impaired relative to control lines (Figure 4 S3), which also aligned with prior observations. These findings strongly indicate that memory loss caused by Dop1R2 flip-out is not due to developmental defects.”
(3) The authors state that they aim to resolve disparities of findings in the field regarding the specific role of Dop1R2 in memory, offering a potent tool to generate mutants and addressing systematically their effects on different types of memory. Their results support the role of this receptor in the expression of long-term memories, however in the experiments performed here do not address temporal resolution of the genetic manipulations that could bring light into the mechanisms of action of Dop1R2 in memory. Several hypotheses have been proposed, from stabilization of memory, effects on forgetting, or integration of sequences of events (sensory experiences and dopamine release).
We thank you for this comment. We agree that it would be interesting to dissect the memory stages by knocking out the receptor selectively in some of them (encoding, consolidation, retrieval). However, our tool irreversibly flips out Dop1R2 preventing us from investigating the receptor’s role in retrieval. Our results show that the receptor is dispensable for STM formation (Figure 2, Figure 4 Supplement 3), suggesting that it is not involved in encoding new information. On the other hand, it is instead involved in consolidation and/or retrieval of long-term and middle-term memories (Figure 3, Figure 4, Figure 5B).
Overall, the authors generated a very useful tool to study dopamine neuromodulation in any given circuit when used in combination with the powerful genetic toolkit available in Drosophila. The reports in this paper confirmed a previously described role of Dop1R2 in the expression of aversive and appetitive LTM and mapped these effects to two specific types of memory neurons in the fly brain, previously implicated in the expression and consolidation of long-term associative memories.
Recommendations for the authors:
Reviewer #1 (Recommendations For The Authors):
(1) On the first view, the results shown here are different from studies published earlier, while in the same line with others (e.g. Sun et al, for appetitive 24h memories). For example, Berry et al showed that the loss of dop1R2 impairs immediate memory, while memory scores are enhanced 3h, 6h, and 24h after training. Further, they showed data that shock avoidance, at least for higher shock intensities, is reduced in mutant (damb) flies. All in all, this favors how important it is to improve the genetic tools for tissue-specific manipulation. Despite the authors nicely discussing their data with respect to the previous studies, I wondered whether it would be suitable to use the new tool and knock out dop1R2 panneuronally to see whether the obtained data match the results published by Berry et al.. Further, as stated in line 105ff: "As these studies used different learning assays - aversive and appetitive respectively as well as different methods, it is unclear if Dop1R2 has different functions for the different reinforcement stimulus" I wondered why the authors tested aversive and appetitive learning for STM and 2h memory, but only appetitive memory for 24h.
Thank you for this comment. To that extent, as mentioned above in response to reviewer #2, we included in the results the aversive LTM experiment (Figure 4). Moreover, we performed experiments along the line of Berry et al. using our tool as shown in Figure 4 S1. Our results support that Dop1R2 is required for LTM, rather than to promote forgetting.
(2) Line 165ff: I can´t find any of the supplementary data mentioned here. Please add the corresponding figures.
Thank you for pointing this out. In that line we don’t refer to any supplementary data, but to the Figure 1F, showing the absence of the HA-tag in our MB knock-out line. We have clarified this in the text (lines 151-153)
(3) I can't imagine that the scale bar in Figure 1D-F is correct. I would also like to suggest to show a more detailed analysis of the expression pattern. For example, both anterior and posterior views would be appropriate, perhaps including the VNC. This would allow the expression pattern obtained with this novel tool to be better compared with previously published results. Also, in relation to my comment above (1), it may help to understand the functional differences with previous studies, especially as the authors themselves state that the receptor is "mainly" expressed in the mushroom body (line 99). It would be interesting to see where else it is expressed (if so). This would also be interesting for the panneuronal knockdown experiment suggested under (1). If the receptor is indeed expressed outside the mushroom body, this may explain the differences to Berry et al.
Thank you for noting this, there was indeed a mistake in the scale bar which we now fixed. Since with our HA-tag immunostaining we could not detect any noticeable signal outside of the MB, we decided to analyze previously existing single cell transcriptomics data that showed expression of the receptor in 7.99% of cells in the VNC and in 13.8% of cells outside the MB (lines 98-100) confirming its sparse expression in the nervous system. The lack of detection of these cells is likely due to the sparse and low expression of the protein. The HA-tag allows to detect the endogenous level of the locus (it is possible that a Gal4/UAS amplification of the signal might allow to detect these cells).
Regarding the panneuronal knockout, we decided to try to replicate the experiment shown in Berry et al. in Figure 4 S1 and found that Dop1R2 is required for LTM.
(4) Related to learning data shown in Figures 2-4, the authors should show statistical differences between all groups obtained in the ANOVA + PostHoc tests. Currently, only an asterisk is placed above the experimental group, which does not adequately reflect the statistical differences between the groups. In addition, I would like to suggest adding statistical tests to the chance level as it may be interesting to know whether, for example, scores of knockout flies in 3C and 3D are different from the chance level.
Many thanks for this correction, we agree with the fact that the way significance scores were shown was not informative enough. We fixed the point by now showing significance between all the control groups and the experimental ones. We also inserted the chance level results in the figure legends.
(5) Unfortunately, the manuscript has some typing errors, so I would like to ask the authors to check the manuscript again carefully.
Some Examples:
Line 31: the the
Line 56: G-Protein
Line 64: c-AMP
Line 68: Dopamine
Line 70: G-Protein (It alternates between G-protein and G-Protein)
Line 76: References are formatted incorrectly
Line 126: Ha-Tag (It alternates between Ha and HA)
Line 248: missing space before the bracket...is often found
Thank you for noticing these errors, we have now corrected the spelling throughout the manuscript.
(6) In the figures the axes are labelled Preference Index (Pref"I"). In the methods, however, the calculation formula is defined as "PREF".
We thank you for drawing attention to this. To avoid confusion, we changed the definition in the methods section so that it could be clear and coherent (“Memory tests” paragraph in the methods section).
“PREF = ((N<sub>arm1</sub> - N<sub>arm2</sub>) 100) / N<sub>total</sub> the two preference indices were calculated from the two reciprocal experiments. The average of these two PREFs gives a learning index (LI). LI = (PREF<sub>1</sub> + PREF<sub>2</sub>) / 2.
In case of all Long-term Aversive memory experiments, Y-Maze protocol was adapted to test flies 24 hours post training. Testing using the Y-Maze was done following the protocol as described in (Mohandasan et al., 2022) where flies were loaded at the bottom of 20-minutes odorized 3D-printed Y-Mazes from where they would climb up to a choice point and choose between the two odors. The learning index was then calculated after counting the flies in each odorized vial as follows: LI = ((N<sub>CS-</sub> - N<sub>CS+</sub>) 100) / N<sub>total</sub>. Where NCS- and NCS+ are the number of flies that were found trapped in the untrained and trained odor tube respectively.
Reviewer #2 (Recommendations For The Authors):
(1) In Figures 2 and 3, the legends running two different subfigures is confusing. Would be helpful to find a different way to present.
Thank you for your suggestion. We modified how we present legends, placing them vertically so that it is clearer.
(2) Use additional drivers to verify middle and long-term memory phenotypes.
We agree that it would be interesting to see the role of Dop1R2 in other neurons. To that extent, we looked at long term aversive memory in flies where the receptor was panneuronaly flipped out, and did not find evidence that suggested involvement of Dop1R2 in memory processes outside the MB. (Figure 4 S1)
(3) Additional discussion of genetic background for fly lines would be helpful.
Thank you for your advice. We have mentioned the genetic background of flies in the key resources table of the methods sections. Additionally, we also included further explanation on how the lines were created and their genetic background (see “Fly Husbandry” paragraph in the methods section).
“UAS-flp;;Dop1R2 cko flies and Gal4;Dop1R2<sup>cko</sup> flies were crossed back with ;;Dop<sup>cko</sup> flies to obtain appropriate genetic controls which were heterozygous for UAS and Gal4 but not Dop1R2<sup>cko</sup>.”
Reviewer #3 (Recommendations For The Authors):
Line 109 states that to resolve the problem a tool is developed to knock down Dop1R2 in s spatial and temporal specific manner- while I agree that this is within the potential of the tool, there is no temporal control of the flipase action in this study; at least I cannot find references to the use of target/gene switch to control stages of development or different memory phases. However the version available for download is missing supplementary information, so I did not have access to supplementary figures and tables.
Thank you for the comment, as mentioned before it would be great to be able to dissect the memory phases. We show in lines 232 – 250 and Figure 4 S3 that the temporally restricted flip-out to the post-eclosion life stage gave us coherent results with the previous findings, ruling out potential developmental defects.
In relation to my comment on the possible developmental effects of the loss of the gene, Figure 1F could showcase an underdeveloped g lobe when looking at the lobe profiles. I understand this is not within the scope of the figure, but maybe a different z projection can be provided to confirm there are no obvious anatomical alterations due to the loss of the receptor.
We understand the doubt about the correct development of the MB and we thank you for your insightful comment. To that extent we decided to perform a FasII immunostaining that could show us the MB in the different lines (Figure 4 S2) and it appears that there are no notable differences in the lobes development in our knockout line.
It seems that the obvious missing piece of the puzzle would be to address the effects of knocking out Dop1R2 in aversive LTM. The idea of systematically addressing different types of memory at different time points and in different KCs is the most attractive aspect of this study beyond the technical sophistication, and it feels that the aim of the study is not delivered without that component.
We agree and we thank you for the clarification. As mentioned above in response to Reviewer #2, we decided to test aversive LTM as described in lines –208-228, Figure 4, Figure 4 S1.
Some statements of the discussion seem too vague, and I think could benefit from editing:
Line 284 "however other receptors could use Gq and mediate forgetting"- does this refer to other dopamine receptors? Other neuromodulators? Examples?
Thank you for pointing this out. We Agree and therefore decided to omit this line.
Line 289 "using a space training protocol and a Dop1R2 line" - this refers to RNAi lines, but it should be stated clearly.
That is correct, we thank you for bringing attention to this and clarified it in the manuscript.
–Lines 329-330
“Interestingly, using a spaced training protocol and a Dop1R2 RNAi knockout line another study showed impaired LTM (Placais et al., 2017).”
The paragraph starting in line 305 could be re-written to improve clarity and flow. Some statements seem disconnected and require specific citations. For example "In aversive memory formation, loss of Dop1R2 could lead to enhanced or impaired memory, depending on the activated signaling pathways and the internal state of the animal...". This is not accurate. Berry et al 2012 report enhanced LTM performance in dop1R2 mutants whereas Plaçais et al 2017 report LTM defects in Dop1R2 knock-downs, but these different findings do not seem to rely on different internal states or signaling pathways. Maybe further elaboration can help the reader understand this speculation.
We agree and we thank you for this advice. We decided to add additional details and citations to validate our speculation
Lines 350-353
“In aversive memory formation, loss of Dop1R2 could lead to enhanced or impaired memory, depending on the activated signaling pathways. The signaling pathway that is activated further depends on the available pool of secondary messengers in the cell (Hermans, 2003) which may be regulated by the internal state of the animal.”
"...for reward memory formation, loss of Dop1R2 seems to impair memory", this seems redundant at this point, as it has been discussed in detail, however, citations should be provided in any case (Musso 2015, Sun 2020)
Thank you for noting this. We recognize the redundancy and decided to exclude the line.
Finally, it would be useful to additionally refer to the anatomical terminology when introducing neuron names; for example MBON MVP2 (MBON-g1pedc>a/b), etc.
Thank you for this suggestion. We understand the importance of anatomical terminologies for the neurons. Therefore, we included them when we introduce neurons in the paper.
We thank you for your observations. We recognize their value, so we have made appropriate changes in the discussion to sound less vague and more comprehensive.
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Reviewer #1 (Public review):
Summary:<br /> This manuscript describes the role of PRDM16 in modulating BMP response during choroid plexus (ChP) development. The authors combine PRDM16 knockout mice and cultured PRDM16 KO primary neural stem cells (NSCs) to determine the interactions between BMP signaling and PRDM16 in ChP differentiation.<br /> They show PRDM16 KO affects ChP development in vivo and BMP4 response in vitro. They determine genes regulated by BMP and PRDM16 by ChIP-seq or CUT&TAG for PRDM16, pSMAD1/5/8, and SMAD4. They then measure gene activity in primary NSCs through H3K4me3 and find more genes are corepressed than coactivated by BMP signaling and PRDM16 and focus on the 31 genes found to be co-repressed by BMP and PRDM16. Wnt7b is in this set and the authors then provide evidence that PRDM16 and BMP signaling together repress Wnt activity in the developing choroid plexus.
Strengths:<br /> Understanding context-dependent response to cell signals during development is an important problem. The authors use a powerful combination of in vivo and in vitro systems to dissect how PRDM16 may modulate BMP response in early brain development.
Main weakness of the experimental setup:<br /> (1) Because the authors state that primary NSCs cultured in vitro lose endogenous Prdm16 expression, they drive expression by a constitutive promoter. However, this means the expression levels is very different from endogenous levels (as explicitly shown in Supp. Fig. 2B) and the effect of many transcription factors is strongly dose-dependent, likely creating differences between the PRDM16-dependent transcriptional response in the in vitro system and in vivo. Although the authors combine in vitro and in vivo evidence on the role of PRDM16 as a co-factor for MBP signaling and verified that BMP induces quiescence in their NSC model in a PRDM16-dependent manner, this experimental setup remains a weakness and likely affects the results of the various genomics experiments.
Other experimental weaknesses that make the evidence less convincing:
(1) It seems that the authors compare Prdm16_KO cells to Prdm16 WT cells overexpressing flag_Prdm16. Aside from the possible expression of endogenous Prdm16, other cell differences may have arisen between these cell lines. A properly controlled experiment would compare Prdm16_KO ctrl (possibly infected with a control vector without Prdm16) to Prdm16_KO_E (i.e. the Prdm16_KO cells with and without Prdm16 overexpression.) The authors acknowledged this problem in their rebuttal, stating that they were unable to overexpress PRDM16 in KO cells.
(2) The authors show in Fig.2E that Ttr is not upregulated by BMP4 in PRDM16_KO NSCs. This appears inconsistent with the presence of Ttr expression in the PRDM16_KO brain in Fig.1C. The authors explained in their rebuttal that the Ttr protein levels are not detectable in the NSCs with antibodies but the effect is still visible at the level of mRNA. The dramatic difference in protein expression is curious.
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Author response:
The following is the authors’ response to the original reviews
Reviewer #1 (Public review):
Summary:
This manuscript describes the role of PRDM16 in modulating BMP response during choroid plexus (ChP) development. The authors combine PRDM16 knockout mice and cultured PRDM16 KO primary neural stem cells (NSCs) to determine the interactions between BMP signaling and PRDM16 in ChP differentiation.
They show PRDM16 KO affects ChP development in vivo and BMP4 response in vitro. They determine genes regulated by BMP and PRDM16 by ChIP-seq or CUT&TAG for PRDM16, pSMAD1/5/8, and SMAD4. They then measure gene activity in primary NSCs through H3K4me3 and find more genes are co-repressed than co-activated by BMP signaling and PRDM16. They focus on the 31 genes found to be co-repressed by BMP and PRDM16. Wnt7b is in this set and the authors then provide evidence that PRDM16 and BMP signaling together repress Wnt activity in the developing choroid plexus.
Strengths:
Understanding context-dependent responses to cell signals during development is an important problem. The authors use a powerful combination of in vivo and in vitro systems to dissect how PRDM16 may modulate BMP response in early brain development.
We thank the reviewer for the thoughtful summary and positive feedback. We appreciate the recognition of our integrative in vivo and in vitro approach. We're glad the reviewer found our findings on context-dependent gene regulation and developmental signaling valuable.
Main weaknesses of the experimental setup:
(1) Because the authors state that primary NSCs cultured in vitro lose endogenous Prdm16 expression, they drive expression by a constitutive promoter. However, this means the expression levels are very different from endogenous levels (as explicitly shown in Supplementary Figure 2B) and the effect of many transcription factors is strongly dose-dependent, likely creating differences between the PRDM16-dependent transcriptional response in the in vitro system and in vivo.
We acknowledge that our in vitro experiments may not ideally replicate the in vivo situation, a common limitation of such experiments, our primary aim was to explore the molecular relationship between PRDM16 and BMP signaling in gene regulation. Such molecular investigations are challenging to conduct using in vivo tissues. In vitro NSCs treated with BMP4 has been used a model to investigate NSC proliferation and quiescence, drawing on previous studies (e.g., Helena Mira, 2010; Marlen Knobloch, 2017). Crucially, to ensure the relevance of our in vitro findings to the in vivo context, we confirmed that cultured cells could indeed be induced into quiescence by BMP4, and this induction necessitated the presence of PRDM16. Furthermore, upon identifying target genes co-regulated by PRDM16 and SMADs, we validated PRDM16's regulatory role on a subset of these genes in the developing Choroid Plexus (ChP) (Fig. 7 and Suppl.Fig7-8). Only by combining evidence from both in vitro and in vivo experiments could we confidently conclude that PRDM16 serves as an essential co-factor for BMP signaling in restricting NSC proliferation.
(2) It seems that the authors compare Prdm16_KO cells to Prdm16 WT cells overexpressing flag_Prdm16. Aside from the possible expression of endogenous Prdm16, other cell differences may have arisen between these cell lines. A properly controlled experiment would compare Prdm16_KO ctrl (possibly infected with a control vector without Prdm16) to Prdm16_KO_E (i.e. the Prdm16_KO cells with and without Prdm16 overexpression.)
We agree that Prdm16 KO cells carrying the Prdm16-expressing vector would be a good comparison with those with KO_vector. However, despite more than 10 attempts with various optimization conditions, we were unable to establish a viable cell line after infecting Prdm16 KO cells with the Prdm16-expressing vector. The overall survival rate for primary NSCs after viral infection is low, and we observed that KO cells were particularly sensitive to infection treatment when the viral vector was large (the Prdm16 ORF is more than 3kb).
As an alternative oo assess vector effects, we instead included two other control cell lines, wt and KO cells infected with the 3xNLS_Flag-tag viral vector, and presented the results in supplementary Fig 2. When we compared the responses of the four lines — wt, KO, wt infected with the Flag vector, KO infected with the Flag vector — to the addition and removal of BMP4, we confirmed that the viral infection itself has no significant impacts on the responses of these cells to these treatments regarding changes in cell proliferation and Ttr induction.
Given that wt cells and the KO cells, with or without viral backbone infection behave quite similarly in terms of cell proliferation, we speculate that even if we were successful in obtaining a cell line with Prdm16-expressing vector in the KO cells, it may not exhibit substantial differences compared to wt cells infected with Prdm16-expressing vector.
Other experimental weaknesses that make the evidence less convincing:
(1) The authors show in Figure 2E that Ttr is not upregulated by BMP4 in PRDM16_KO NSCs. Does this appear inconsistent with the presence of Ttr expression in the PRDM16_KO brain in Figure1C?
The reviwer’s point is that there was no significant increase in Ttr expression in Prdm16_KO cells after BMP4 treatment (Fig. 2E), but there remained residule Ttr mRNA signals in the Prdm16 mutant ChP (Fig. 1C). We think the difference lies in the measuable level of Ttr expression between that induced by BMP4 in NSC culture and that in the ChP. This is based on our immunostaining expreriment in which we tried to detect Ttr using a Ttr antibody. This antibody could not detect the Ttr protein in BMP4-treated Prdm16_expressing NSCs but clearly showed Ttr signal in the wt ChP. This means that although Ttr expression can be significantly increased by BMP4 in vitro to a level measurable by RT-qPCR, its absolute quantity even in the Prdm16_expressing condition is much lower compared to that in vivo. Our results in Fig 1C and Fig 2E, as well as Fig 7B, all consistently showed that Prdm16 depletion significantly reduced Ttr expression in in vitro and in vivo.
(2) Figure 3: The authors use H3K4me3 to measure gene activity. This is however, very indirect, with bulk RNA-seq providing the most direct readout and polymerase binding (ChIP-seq) another more direct readout. Transcription can be regulated without expected changes in histone methylation, see e.g. papers from Josh Brickman. They verify their H3K4me3 predictions with qPCR for a select number of genes, all related to the kinetochore, but it is not clear why these genes were picked, and one could worry whether these are representative.
H3K4me3 has widely been used as an indicator of active transcription and is a mark for cell identity genes. And it has been demonstrated that H3K4me3 has a direct function in regulating transciption at the step of RNApolII pausing release. As stated in the text, there are advantages and disadvantages of using H3K4me3 compared to using RNA-seq. RNA-seq profiles all gene products, which are affected by transcription and RNA stability and turnover. In contrast, H3K4me3 levels at gene promoter reflects transcriptional activity. In our case, we aimed to identify differential gene expression between proliferation and quiescence states. The transition between these two states is fast and dynamic. RNA-seq may not be able to identify functionally relevant genes but more likely produces false positive and negative results. Therefore, we chose H3K4me3 profiling.
We agree that transcription may change without histone methylation changes. This may cause an under-estimation of the number of changed genes between the conditions.
We validated 7 out of 31 genes (Wnt7b, Id3, Mybl2, Spc24, Spc25, Ndc80 and Nuf2). We chose these genes based on two critira: 1) their function is implicated in cell proliferation and cell-cycle regulation based on gene ontology analysis; 2) their gene products are detectable in the developing ChP based on the scRNA-seq data. Three of these genes (Wnt7b, Id3, Mybl2) are not related to the kinetochore. We now clarify this description in the revised text.
(3) Line 256: The overlap of 31 genes between 184 BMP-repressed genes and 240 PRDM16-repressed genes seems quite small.
This result indicates that in addition to co-repressing cell-cycle genes, BMP and PRDM16 have independent fucntions. For example, it was reported that BMP regulates neuronal and astrocyte differentiation (Katada, S. 2021), while our previous work demonstrated that Prdm16 controls temporal identity of NSCs (He, L. 2021).
(4) The Wnt7b H3K4me3 track in Fig. 3G is not discussed in the text but it shows H3K4me3 high in _KO and low in _E regardless of BMP4. This seems to contradict the heatmap of H3K4me3 in Figure 3E which shows H3K4me3 high in _E no BMP4 and low in _E BMP4 while omitting _KO no BMP4. Meanwhile CDKN1A, the other gene shown in 3G, is missing from 3E.
The track in Fig 3G shows the absolute signal of H3K4me3 after mapping the sequencing reads to the genome and normaliz them to library size. Compare the signal in Prdm16_E with BMP4 and that in Prdm16_E without BMP4, the one with BMP4 has a lower peak. The same trend can be seen for the pair of Prdm16_KO cells with or without BMP4. The heatmap in Fig. 3E shows the relative level of H3K4me3 in three conditions. The Prdm16_E cells with BMP4 has the lowest level, while the other two conditions (Prdm16_KO with BMP4 and Prdm16_E without BMP4) display higher levels. These two graphs show a consistent trend of H3K4me3 changes at the Wnt7b promoter across these conditions. Figure 3E only includes genes that are co-repressed by PRDM16 and BMP. CDKN1A’s H3K4me3 signals are consistent between the conditions, and thus it is not a PRDM16- or BMP-regulated gene. We use it as a negative control.
(5) The authors use PRDM16 CUT&TAG on dissected dorsal midline tissues to determine if their 31 identified PRDM16-BMP4 co-repressed genes are regulated directly by PRDM16 in vivo. By manual inspection, they find that "most" of these show a PRDM16 peak. How many is most? If using the same parameters for determining peaks, how many genes in an appropriately chosen negative control set of genes would show peaks? Can the authors rigorously establish the statistical significance of this observation? And why wasn't the same experiment performed on the NSCs in which the other experiments are done so one can directly compare the results? Instead, as far as I could tell, there is only ChIP-qPCR for two genes in NSCs in Supplementary Figure 4D.
In our text, we indicated the genes containing PRDM16 binding peaks in the figures and described them as “Text in black in Fig. 6A and Supplementary Fig. 5A”. We will add the precise number “25 of these genes” in the main text to clarify it. We used BMP-only repressed 184-31 =153 genes (excluding PRDM16-BMP4 co-repressed) as a negative control set of genes. By computationally determine the nearest TSS to a PRDM16 peak, we identified 24/31 co-repressed genes and 84/153 BMP-only-repressed genes, containing PRDM16 peaks in the E12.5 ChP data. Fisher’s Exact Test comparing the proportions yields the P-value = 0.015.
We are confused with the second part of the comment “And why wasn't the same experiment performed on the NSCs in which the other experiments are done so one can directly compare the results? Instead, as far as I could tell, there is only ChIP-qPCR for two genes in NSCs in Supplementary Figure 4D.” If the reviewer meant why we didn’t sequence the material from sequential-ChIP or validate more taget genes, the reason is the limitation of the material. Sequential ChIP requires a large quantity of the antibodies, and yields little material barely sufficient for a few qPCR after the second round of IP. This yielded amount was far below the minimum required for library construction. The PRDM16 antibody was a gift, and the quantity we have was very limited. We made a lot of efforts to optimize all available commercial antibodies in ChIP and Cut&Tag, but none of them worked in these assays.
(6) In comparing RNA in situ between WT and PRDM16 KO in Figure 7, the authors state they use the Wnt2b signal to identify the border between CH and neocortex. However, the Wnt2b signal is shown in grey and it is impossible for this reviewer to see clear Wnt2b expression or where the boundaries are in Figure 7A. The authors also do not show where they placed the boundaries in their analysis. Furthermore, Figure 7B only shows insets for one of the regions being compared making it difficult to see differences from the other region. Finally, the authors do not show an example of their spot segmentation to judge whether their spot counting is reliable. Overall, this makes it difficult to judge whether the quantification in Figure 7C can be trusted.
In the revised manuscript we have included an individal channel of Wnt2b and mark the boundaries. We also provide full-view images and examples of spot segmentation in the new supplementary figure 8.
(7) The correlation between mKi67 and Axin2 in Figure 7 is interesting but does not convincingly show that Wnt downstream of PRDM16 and BMP is responsible for the increased proliferation in PRDM16 mutants.
We agree that this result (the correlation between mKi67 and Axin2) alone only suggests that Wnt signaling is related to the proliferation defect in the Prdm16 mutant, and does not necessarily mean that Wnt is downstream of PRDM16 and BMP. Our concolusion is backed up by two additional lines of evidences: the Cut&Tag data in which PRDM16 binds to regulatory regions of Wnt7b and Wnt3a; BMP and PRDM16 co-repress Wnt7b in vitro.
An ideal result is that down-regulating Wnt signaling in Prdm16 mutant can rescue Prdm16 mutant phenotype. Such an experiment is technically challenging. Wnt plays diverse and essential roles in NSC regulation, and one would need to use a celltype-and stage-specific tool to down-regulate Wnt in the background of Prdm16 mutation. Moreover, Wnt genes are not the only targets regulated by PRDM16 in these cells, and downregulating Wnt may not be sufficient to rescue the phenotype.
Weaknesses of the presentation:
Overall, the manuscript is not easy to read. This can cause confusion.
We have revised the text to improve clarity.
Reviewer #1 (Recommendations for the authors):
(1) Overall, the manuscript is not easy to read. Here are some causes of confusion for which the presentation could be cleaned up:
We are grateful for the reviewer’s suggestion. In the revised manuscript, we have made efforts to improve the clarity of the text.
(a) Part of the first section is confusing in that some statements seem contradictory, in particular:
"there is no overall patterning defect of ChP and CH in the Prdm16 mutant" (line 125)
"Prdm16 depletion disrupted the transition from neural progenitors into ChP epithelia" (line 144)
It would be helpful if the authors could reformulate this more clearly.
We modified the text to clarify that while the BMP-patterned domain is not affected, the transition of NSCs into ChP epithelial cells is compromised in the Prdm16 mutant.
(b) Flag_PRDM16, PRDM16_expressing, PRDM16_E, PRDM16 OE all seem to refer to the same PRDM16 overexpressing cells, which is very confusing. The authors should use consistent naming. Moreover, it would be good if they renamed these all to PRDM16_OE to indicate expression is not endogenous but driven by a constitutive promoter.
We appreciate the comment and agree that the use of multiple terms to refer to the same PRDM16-overexpressing condition was confusing. Our original intention in using Prdm16_E was to distinguish cells expressing PRDM16 from the two other groups: wild-type cells and Prdm16_KO cells, which both lack PRDM16 protein expression. However, we acknowledge that Prdm16_E could be misinterpreted as indicating expression from the endogenous Prdm16 promoter. To avoid this confusion and ensure consistency, we have now standardized the terminology and refer to this condition as Prdm16_OE, indicating Flag-tagged PRDM16 expression driven by a constitutive promoter.
(c) Line 179 states "generated a cell line by infecting Prdm16_KO cells with the same viral vector, expressing 3xNSL_Flag". Do the authors mean 3xNLS_Flag_Prdm16, so these are the Prdm16_KO_E cells by the notation suggested above? Or is this a control vector with Flag only? The following paragraph refers to Supplementary Figure 2C-F where the same construct is called KO_CDH, suggesting this was an empty CDH vector, without Flag, or Prdm16. This is confusing.
We appreciate the reviewer’s careful reading and helpful comment. We acknowledge the confusion caused by the inconsistent terminology. To clarify: in line 179, we intended to describe an attempt to generate a Prdm16_KO cell line expressing 3xNLS_Flag_Prdm16, not a control vector with Flag only. However, despite repeated attempts, we were unable to establish this line due to low viral efficiency and the vulnerability of Prdm16_KO cells to infection with the large construct. Therefore, these cells were not included in the subsequent analyses.
The term KO_CDH refers to Prdm16_KO cells infected with the empty CDH control vector, which lacks both Flag and Prdm16. This is the line used in the experiments shown in Supplementary Fig. 2C–F. We have revised the text throughout the manuscript to ensure consistent use of terminology and to avoid this confusion.
(2) The introductory statements on lines 53-54 could use more references.
Thanks for the suggestion. We have now included more references.
(3) It would be helpful if all structures described in the introduction and first section were annotated in Figure 1, or otherwise, if a cartoon were included. For example, the cortical hem, and fourth ventricle.
Thanks for the suggestion. We have now indicated the structures, ChP, CH and the fourth ventricle, in the images in Figure 1 and Supplementary Figure 1.
(4) In line 115, "as previously shown.." - to keep the paper self-contained a figure illustrating the genetics of the KO allele would be helpful.
Thanks for the suggestion. We have now included an illustration of the Prdm16 cGT allele in Figure 1B.
(5) In Figure 1D as costain for a ChP marker would be helpful because it is hard to identify morphologically in the Prdm16 KO.
Appoligize for the unclarity. The KO allele contains a b-geo reporter driven by Prdm16 endogenous promoter. The samples were co-stained for EdU, b-Gal and DAPI. To distingquish the ChP domain from the CH, we used the presence of b b-Gal as a marker. We indicated this in the figure legend, but now have also clarified this in the revised text.
(6) The details in Figure 1E are hard to see, a zoomed-in inset would help.
A zoomed-in inset is now included in the figure.
(7) Supplementary Figure 2A does not convincingly show that PRDM16 protein is undetectable since endogenous expression may be very low compared to the overexpression PRDM16_E cells so if the contrast is scaled together it could appear black like the KO.
We appreciate the reviewer’s point and have carefully considered this concern. We concluded that PRDM16 protein is effectively undetectable in cultured wild-type NSCs based on direct comparison with brain tissue. Both cultured NSCs and brain sections were processed under similar immunostaining and imaging conditions. While PRDM16 showed robust and specific nuclear localization in embryonic brain sections (Fig. 1B and Supplementary Fig. 1A), only a small subset of cultured NSCs exhibited PRDM16 signal, primarily in the cytoplasm (middle panel of Fig. 2A). This stark contrast supports our conclusion that endogenous PRDM16 protein is either absent or significantly downregulated in vitro. Because of this limitation, we turned to over-expressing Prdm16 in NSC culture using a constitutive promoter.
(9) Line 182 "Following the washout step" - no such step had been described, maybe replace by "After washout of BMP".
Yes, we have revised the text.
(8) Line 214: "indicating a modest level" - what defines modest? Compared to what? Why is a few thousand moderate rather than low? Does it go to zero with inhibitors for pathways?
Here a modest level means a lower level than to that after adding BMP4. To clarify this, we revised the description to “indicating endogenous levels of …”
(9) The way qPCR data are displayed makes it difficult to appreciate the magnitude of changes, e.g. in Supplementary Figure 2B where a gap is introduced on the scale. Displaying log fold change / relative CT values would be more informative.
We used a segmented Y-axis in Supplementary Figure 2B because the Prdm16 overexpression samples exhibited much higher experssion levels compared to other conditions. In response to this suggestion, we explored alternative ways to present the result, including ploting log-transformed values and log fold changes. However, these methods did not enhance the clarity of the differences – in fact, log scaling made the magnitude of change appear less apparent. To address this, we now present the overexpression samples in a separate graph, thereby eliminating the need for a broken Y-axis and improving the overall readability of the data.
(10) Writing out "3 days" instead of 3D in Figure 2A would improve clarity. It would be good if the used time interval is repeated in other figures throughout the paper so it is still clear the comparison is between 0 and 3 days.
We have changed “3D” to “3 days”. All BMP4 treatments in this study were 3 days.
(11) Line 290: "we found that over 50% of SMAD4 and pSMAD1/5/8 binding peaks were consistent in Prdm16_E and Prdm16_KO cells, indicating that deletion of Prdm16 does not affect the general genomic binding ability of these proteins" - this only makes sense to state with appropriate controls because 50% seems like a big difference, what is the sample to sample variability for the same condition? Moreover, the next paragraph seems to contradict this, ending with "This result suggests that SMAD binding to these sites depends on PRDM16". The authors should probably clarify the writing.
We appreciate the reviwer’s comment and agree that clarification was needed. Our point was that SMAD4 and pSMAD1/5/8 retain the ability to bind DNA broadly in the Prdm16 KO cells, with more than half of the original binding sites still occupied. This suggests that deletion of Prdm16 does not globally impair SMAD genomic binding. Howerever, our primary interest lies in the subset of sites that show differential by SMAD binding between wt and Prdm16 KO conditions, as thse are likely to be PRDM16-dependent.
In the following paragraph, we focused specifically on describing SMAD and PRDM16 co-bound sites. At these loci, SMAD4 and pSMAD1/5/8 showed reduced enrichment in the absence of PRDM16, suggesting PRDM16 facilitates SMAD binding at these particular regions. We have revised the text in the manuscript to more clearly distinguish between global SMAD binding and PRDM16-dependent sites.
(12) Much more convincing than ChIP-qPCR for c-FOS for two loci in Figures 5F-G would be a global analysis of c-FOS ChIP-seq data.
We agree that a global c-FOS ChIP-seq analysis would provide a more comprehensive view of c-FOS binding patterns. However, the primary focus of this study is the interaction between BMP signaling and PRDM16. The enrichment of AP-1 motifs at ectopic SMAD4 binding sites was an unexpected finding, which we validated using c-FOS ChIP-qPCR at selected loci. While a genome-wide analysis would be valuable, it falls beyond the current scope. We agree that future studies exploring the interplay among SMAD4/pSMAD, PRDM16, and AP-1 will be important and informative.
(13) Figure 6A is hard to read. A heatmap would make it much easier to see differences in expression. Furthermore, if the point is to see the difference between ChP and CH, why not combine the different subclusters belonging to those structures? Finally, why are there 28 genes total when it is said the authors are evaluating a list of 31 genes and also displaying 6 genes that are not expressed (so the difference isn't that unexpressed genes are omitted)?
For the scRNA-seq data, we chose violin plots because they display both gene expression levels and the number of cells that express each gene. However, we agree that the labels in Figure 6A were too small and difficult to read. We have revised the figure by increasing the font size and moved genes with low expression to Supplementary Figure 5A. Figure 6A includes 17 more highly expressed genes together with three markers, and Supplementary Figure 5A contains 13 lowly expressed genes. One gene Mrtfb is missing in the scRNA-seq data and thus not included. We have revised the description of the result in the main text and figure legends.
Reviewer #2 (Public review):
Summary:
This article investigates the role of PRDM16 in regulating cell proliferation and differentiation during choroid plexus (ChP) development in mice. The study finds that PRDM16 acts as a corepressor in the BMP signaling pathway, which is crucial for ChP formation.
The key findings of the study are:
(1) PRDM16 promotes cell cycle exit in neural epithelial cells at the ChP primordium.
(2) PRDM16 and BMP signaling work together to induce neural stem cell (NSC) quiescence in vitro.
(3) BMP signaling and PRDM16 cooperatively repress proliferation genes.
(4) PRDM16 assists genomic binding of SMAD4 and pSMAD1/5/8.
(5) Genes co-regulated by SMADs and PRDM16 in NSCs are repressed in the developing ChP.
(6) PRDM16 represses Wnt7b and Wnt activity in the developing ChP.
(7) Levels of Wnt activity correlate with cell proliferation in the developing ChP and CH.
In summary, this study identifies PRDM16 as a key regulator of the balance between BMP and Wnt signaling during ChP development. PRDM16 facilitates the repressive function of BMP signaling on cell proliferation while simultaneously suppressing Wnt signaling. This interplay between signaling pathways and PRDM16 is essential for the proper specification and differentiation of ChP epithelial cells. This study provides new insights into the molecular mechanisms governing ChP development and may have implications for understanding the pathogenesis of ChP tumors and other related diseases.
Strengths:
(1) Combining in vitro and in vivo experiments to provide a comprehensive understanding of PRDM16 function in ChP development.
(2) Uses of a variety of techniques, including immunostaining, RNA in situ hybridization, RT-qPCR, CUT&Tag, ChIP-seq, and SCRINSHOT.
(3) Identifying a novel role for PRDM16 in regulating the balance between BMP and Wnt signaling.
(4) Providing a mechanistic explanation for how PRDM16 enhances the repressive function of BMP signaling. The identification of SMAD palindromic motifs as preferred binding sites for the SMAD/PRDM16 complex suggests a specific mechanism for PRDM16-mediated gene repression.
(5) Highlighting the potential clinical relevance of PRDM16 in the context of ChP tumors and other related diseases. By demonstrating the crucial role of PRDM16 in controlling ChP development, the study suggests that dysregulation of PRDM16 may contribute to the pathogenesis of these conditions.
We thank the reviewer for the thorough and thoughtful summary of our study. We’re glad the key findings and significance of our work were clearly conveyed, particularly regarding the role of PRDM16 in coordinating BMP and Wnt signaling during ChP development. We also appreciate the recognition of our integrated approach and the potential implications for understanding ChP-related diseases.
Weaknesses:
(1) Limited investigation of the mechanism controlling PRDM16 protein stability and nuclear localization in vivo. The study observed that PRDM16 protein became nearly undetectable in NSCs cultured in vitro, despite high mRNA levels. While the authors speculate that post-translational modifications might regulate PRDM16 in NSCs similar to brown adipocytes, further investigation is needed to confirm this and understand the precise mechanism controlling PRDM16 protein levels in vivo.
While mechansims controlling PRDM16 protein stability and nuclear localization in the developing brain are interesting, the scope of this paper is revealing the function of PRDM16 in the choroid plexus and its interaction with BMP signaling. We will be happy to pursuit this direction in our next study.
(2) Reliance on overexpression of PRDM16 in NSC cultures. To study PRDM16 function in vitro, the authors used a lentiviral construct to constitutively express PRDM16 in NSCs. While this approach allowed them to overcome the issue of low PRDM16 protein levels in vitro, it is important to consider that overexpressing PRDM16 may not fully recapitulate its physiological role in regulating gene expression and cell behavior.
As stated above, we acknowledge that findings from cultured NSCs may not directly apply to ChP cells in vivo. We are cautious with our statements. The cell culture work was aimed to identify potential mechanisms by which PRDM16 and SMADs interact to regulate gene expression and target genes co-regulated by these factors. We expect that not all targets from cell culture are regulated by PRDM16 and SMADs in the ChP, so we validated expression changes of several target genes in the developing ChP and now included the new data in Fig. 7 and Supplementary Fig. 7. Out of the 31 genes identified from cultured cells, four cell cycle regulators including Wnt7b, Id3, Spc24/25/nuf2 and Mybl2, showed de-repression in Prdm16 mutant ChP. These genes can be relevant downstream genes in the ChP, and other target genes may be cortical NSC-specific or less dependent on Prdm16 in vivo.
(3) Lack of direct evidence for AP1 as the co-factor responsible for SMAD relocation in the absence of PRDM16. While the study identified the AP1 motif as enriched in SMAD binding sites in Prdm16 knockout cells, they only provided ChIP-qPCR validation for c-FOS binding at two specific loci (Wnt7b and Id3). Further investigation is needed to confirm the direct interaction between AP1 and SMAD proteins in the absence of PRDM16 and to rule out other potential co-factors.
We agree that the finding of the AP1 motif enriched at the PRDM16 and SMAD co-binding regions in Prdm16 KO cells can only indirectly suggest AP1 as a co-factor for SMAD relocation. That’s why we used ChIP-qPCR to examine the presence of C-fos at these sites. Although we only validated two targets, the result confirms that C-fos binds to the sites only in the Prdm16 KO cells but not Prdm16_expressing cells, suggesting AP1 is a co-factor. Our results cannot rule out the presence of other co-factors.
Reviewer #2 (Recommendations for the authors):
Minor typo: [7, page 3] "sicne" should be "since".
We appreciate the reviewer’s careful reading. We have now corrected the typo and revised some part of the text to improve clarity.
Reviewer #3 (Public review):
Summary:
Bone morphogenetic protein (BMP) signaling instructs multiple processes during development including cell proliferation and differentiation. The authors set out to understand the role of PRDM16 in these various functions of BMP signaling. They find that PRDM16 and BMP co-operate to repress stem cell proliferation by regulating the genomic distribution of BMP pathway transcription factors. They additionally show that PRDM16 impacts choroid plexus epithelial cell specification. The authors provide evidence for a regulatory circuit (constituting of BMP, PRDM16, and Wnt) that influences stem cell proliferation/differentiation.
Strengths:
I find the topics studied by the authors in this study of general interest to the field, the experiments well-controlled and the analysis in the paper sound.
We thank the reviewer for their positive feedback and thoughtful summary. We appreciate the recognition of our efforts to define the role of PRDM16 in BMP signaling and stem cell regulation, as well as the soundness of our experimental design and analysis.
Weaknesses:
I have no major scientific concerns. I have some minor recommendations that will help improve the paper (regarding the discussion).
We have revised the discussion according to the suggestions.
Reviewer #3 (Recommendations for the authors):
Specific minor recommendations:
Page 18. Line 526: In a footnote, the authors point out a recent report which in parallel was investigating the link between PRDM16 and SMAD4. There is substantial non-overlap between these two papers. To aid the reader, I would encourage the authors to discuss that paper in the discussion section of the manuscript itself, highlighting any similarities/differences in the topic/results.
Thanks for the suggestion. We now included the comparison in the discussion. One conclusion between our study and this publication is consistent, that PRDM16 functions as a co-repressor of SMAD4. However, the mechanims are different. Our data suggests a model in which PRDM16 facilitates SMAD4/pSMAD binding to repress proliferation genes under high BMP conditions. However, the other report suggests that SMAD4 steadily binds to Prdm16 promoter and switches regulatory functions depending on the co-factors. Together with PRDM16, SMAD4 represses gene expression, while with SMAD3 in response to high levels of TGF-b1, it activates gene expression. These differences could be due to different signaling (BMP versus TGF-b), contexts (NSCs versus Pancreatic cancers) etc.
Page 3. Line 65: typo 'since'
We appreciate the reviewer’s careful reading. We have now corrected the typo and revised the text to improve clarity.
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Perform oral prophylaxis procedure using nonfluoridated and oil less prophylaxis pastes.• Clean and wash the teeth with water. Isolate to prevent any contamination from salivaor gingival crevicular fluid• Apply acid etchant in the form of gel for 15 to 30 seconds. Deciduous teeth requirelonger time for etching than permanent teeth because of the presence of aprismaticenamel in deciduous teeth• Wash the etchant continuously for 10 to 15 seconds• Note the appearance of a properly etched surface. It should give a frosty whiteappearance on drying• If any sort of contamination occurs, repeat the procedure• Now apply bonding agent and low viscosity monomers over the etched enamel surface.Generally, bonding agents contain Bis-GMA or UDMA with TEGDMA added to lower theviscosity of the bonding agent. The bonding agents due to their low viscosity, rapidly wetand penetrate the clean, dried, conditioned enamel into the microspaces forming resintags. The resin tags which form between enamel prisms are known as Macrotags.
① Perform oral prophylaxis procedure using nonfluoridated and oil less prophylaxis pastes. ① Florürsüz ve yağsız profilaksi patları kullanarak ağız hijyen uygulaması yapın.
② Clean and wash the teeth with water. Isolate to prevent any contamination from saliva or gingival crevicular fluid ② Dişleri suyla temizleyip yıkayın. Tükürük veya diş eti oluğu sıvısından gelebilecek bulaşmaları önlemek için izolasyon sağlayın.
③ Apply acid etchant in the form of gel for 15 to 30 seconds. Deciduous teeth require longer time for etching than permanent teeth because of the presence of aprismatic enamel in deciduous teeth ③ Asit ajanı jel formunda 15 ila 30 saniye süreyle uygulayın. Süt dişlerinde aprismatik mine bulunduğu için, daimi dişlere göre daha uzun süre asitlenmeleri gerekir.
④ Wash the etchant continuously for 10 to 15 seconds ④ Asit ajanı sürekli şekilde 10 ila 15 saniye boyunca yıkayın.
⑤ Note the appearance of a properly etched surface. It should give a frosty white appearance on drying ⑤ Uygun şekilde asitlenmiş yüzeyin görünümüne dikkat edin. Kuruduğunda buzlu beyaz bir görünüm vermelidir.
⑥ If any sort of contamination occurs, repeat the procedure ⑥ Herhangi bir kontaminasyon meydana gelirse işlemi tekrarlayın.
⑦ Now apply bonding agent and low viscosity monomers over the etched enamel surface. ⑦ Şimdi, asitlenmiş mine yüzeyine bağlayıcı ajan ve düşük viskoziteli monomerleri uygulayın.
⑧ Generally, bonding agents contain Bis-GMA or UDMA with TEGDMA added to lower the viscosity of the bonding agent. ⑧ Genellikle bağlayıcı ajanlar, viskoziteyi azaltmak için TEGDMA ile birlikte Bis-GMA veya UDMA içerir.
⑨ The bonding agents due to their low viscosity, rapidly wet and penetrate the clean, dried, conditioned enamel into the microspaces forming resin tags. ⑨ Bağlayıcı ajanlar düşük viskoziteleri nedeniyle temizlenmiş, kurutulmuş ve hazırlanmış mineyi hızla ıslatır ve mikro boşluklara nüfuz ederek rezin çıkıntılar (resin tag) oluştururlar.
⑩ The resin tags which form between enamel prisms are known as Macrotags. ⑩ Mine prizmaları arasında oluşan rezin çıkıntılara makrotag (macrotag) adı verilir.
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www.medrxiv.org www.medrxiv.org
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Author response:
Our response aims to address the following:
The lack of pleiotropy is an unconfirmable assumption of MR, and the addition of those models is therefore quite important, as this is a primary weakness of the MR approach. Given that concern, I read the sensitivity analyses using pleiotropy-robust models as the main result, and in that case, they can't test their hypotheses as these models do not show a BMI instrumental variable association. The other weakness, which might be remedied, is that the power of the tests here is not described. When a hypothesis is tested with an under-powered model, the apparent lack of association could be due to inadequate sample size rather than a true null. Typically, when a statistically significant association is reported, power concerns are discounted as long as the study is not so small as to create spurious findings. That is the case with their primary BMI instrumental variable model - they find an association so we can presume it was adequately powered. But the primary models they share are not the pleiotropy-robust methods MR-Egger, weighted median, and weighted mode. The tests for these models are null, and that could mean a couple of things: (1) the original primary significant association between the BMI genetic instrument was due to pleiotropy, and they therefore don't have a robust model to explore the effects of the tobacco genetic instrument. (2) The power for the sensitivity analysis models (the pleiotropy-robust methods) is inadequate, and the authors share no discussion about the relative power of the different MR approaches. If they do have adequate power, then again, there is no need to explore the tobacco instrument.
We would like to highlight that post-hoc power calculations are often considered redundant since the statistical power estimated for an observed association is directly related to its p-value[1]. In other words, the uncertainty of the association is already reflected in its 95% confidence interval. However, we understand power calculations may still be of interest to the reader, so we will incorporate them in the revised manuscript.
The reason we use inverse variance weighted (IVW) Mendelian randomization (MR) to obtain our main results rather than the pleiotropy-robust methods mentioned by the reviewer/editors (i.e., MR-Egger, weighted median and weighted mode) is that the former has greater statistical power than the latter[2]. Hence, instead of focussing on the statistical significance of the pleiotropy-robust analyses, we consider it is of more value to compare the consistency of the effect sizes and direction of the effect estimates across methods. Any evidence of such consistency increases our confidence in our main findings, since each method relies on different assumptions. As we cannot be sure about the presence and nature of horizontal pleiotropy, it is useful to compare results across methods even though they are not equally powered. It is true that our results for the genetically predicted effects of body mass index (BMI) on the risk of head and neck cancer (HNC) differ across methods. This is precisely what led us to question the validity of our main finding (suggesting a positive effect of BMI on HNC risk). We will clarify this in the discussion section of the revised manuscript as advised.
We understand that the reviewer/editors are concerned that we do not have a robust model to explore the role of tobacco consumption in the link between BMI and HNC. However, we have a different perspective on the matter. If indeed, the main IVW finding for BMI and HNC is due to pleiotropy (since some of the pleiotropy-robust methods suggest conflicting results), then the IVW multivariable MR method is a way to explore the potential source of this bias[3]. We were particularly interested in exploring the role of smoking in the observed association because smoking and adiposity are known to influence each other [4-9] and share a genetic basis[10, 11].
References:
(1) Heinsberg LW, Weeks DE: Post hoc power is not informative. Genet Epidemiol 2022, 46(7):390-394.
(2) Burgess S, Butterworth A, Thompson SG: Mendelian randomization analysis with multiple genetic variants using summarized data. Genet Epidemiol 2013, 37(7):658-665.
(3) Burgess S, Davey Smith G, Davies NM, Dudbridge F, Gill D, Glymour MM, Hartwig FP, Kutalik Z, Holmes MV, Minelli C et al: Guidelines for performing Mendelian randomization investigations: update for summer 2023. Wellcome Open Res 2019, 4:186.
(4) Morris RW, Taylor AE, Fluharty ME, Bjorngaard JH, Asvold BO, Elvestad Gabrielsen M, Campbell A, Marioni R, Kumari M, Korhonen T et al: Heavier smoking may lead to a relative increase in waist circumference: evidence for a causal relationship from a Mendelian randomisation meta-analysis. The CARTA consortium. BMJ Open 2015, 5(8):e008808.
(5) Taylor AE, Morris RW, Fluharty ME, Bjorngaard JH, Asvold BO, Gabrielsen ME, Campbell A, Marioni R, Kumari M, Hallfors J et al: Stratification by smoking status reveals an association of CHRNA5-A3-B4 genotype with body mass index in never smokers. PLoS Genet 2014, 10(12):e1004799.
(6) Taylor AE, Richmond RC, Palviainen T, Loukola A, Wootton RE, Kaprio J, Relton CL, Davey Smith G, Munafo MR: The effect of body mass index on smoking behaviour and nicotine metabolism: a Mendelian randomization study. Hum Mol Genet 2019, 28(8):1322-1330.
(7) Asvold BO, Bjorngaard JH, Carslake D, Gabrielsen ME, Skorpen F, Smith GD, Romundstad PR: Causal associations of tobacco smoking with cardiovascular risk factors: a Mendelian randomization analysis of the HUNT Study in Norway. Int J Epidemiol 2014, 43(5):1458-1470.
(8) Carreras-Torres R, Johansson M, Haycock PC, Relton CL, Davey Smith G, Brennan P, Martin RM: Role of obesity in smoking behaviour: Mendelian randomisation study in UK Biobank. BMJ 2018, 361:k1767.
(9) Freathy RM, Kazeem GR, Morris RW, Johnson PC, Paternoster L, Ebrahim S, Hattersley AT, Hill A, Hingorani AD, Holst C et al: Genetic variation at CHRNA5-CHRNA3-CHRNB4 interacts with smoking status to influence body mass index. Int J Epidemiol 2011, 40(6):1617-1628.
(10) Thorgeirsson TE, Gudbjartsson DF, Sulem P, Besenbacher S, Styrkarsdottir U, Thorleifsson G, Walters GB, Consortium TAG, Oxford GSKC, consortium E et al: A common biological basis of obesity and nicotine addiction. Transl Psychiatry 2013, 3(10):e308.
(11) Wills AG, Hopfer C: Phenotypic and genetic relationship between BMI and cigarette smoking in a sample of UK adults. Addict Behav 2019, 89:98-103.
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Author response:
The following is the authors’ response to the original reviews
Public Reviews:
Reviewer #1 (Public review):
Summary:
In this manuscript, Azlan et al. identified a novel maternal factor called Sakura that is required for proper oogenesis in Drosophila. They showed that Sakura is specifically expressed in the female germline cells. Consistent with its expression pattern, Sakura functioned autonomously in germline cells to ensure proper oogenesis. In Sakura KO flies, germline cells were lost during early oogenesis and often became tumorous before degenerating by apoptosis. In these tumorous germ cells, piRNA production was defective and many transposons were derepressed. Interestingly, Smad signaling, a critical signaling pathway for GSC maintenance, was abolished in sakura KO germline stem cells, resulting in ectopic expression of Bam in whole germline cells in the tumorous germline. A recent study reported that Bam acts together with the deubiquitinase Otu to stabilize Cyc A. In the absence of sakura, Cyc A was upregulated in tumorous germline cells in the germarium. Furthermore, the authors showed that Sakura co-immunoprecipitated Otu in ovarian extracts. A series of in vitro assays suggested that the Otu (1-339 aa) and Sakura (1-49 aa) are sufficient for their direct interaction. Finally, the authors demonstrated that the loss of otu phenocopies the loss of sakura, supporting their idea that Sakura plays a role in germ cell maintenance and differentiation through interaction with Otu during oogenesis.
Strengths:
To my knowledge, this is the first characterization of the role of CG14545 genes. Each experiment seems to be well-designed and adequately controlled.
Weaknesses:
However, the conclusions from each experiment are somewhat separate, and the functional relationships between Sakura's functions are not well established. In other words, although the loss of Sakura in the germline causes pleiotropic effects, the cause-and-effect relationships between the individual defects remain unclear.
Reviewer #2 (Public review):
In this study, the authors identified CG14545 (and named it Sakura), as a key gene essential for Drosophila oogenesis. Genetic analyses revealed that Sakura is vital for both oogenesis progression and ultimate female fertility, playing a central role in the renewal and differentiation of germ stem cells (GSC).
The absence of Sakura disrupts the Dpp/BMP signaling pathway, resulting in abnormal bam gene expression, which impairs GSC differentiation and leads to GSC loss. Additionally, Sakura is critical for maintaining normal levels of piRNAs. Also, the authors convincingly demonstrate that Sakura physically interacts with Otu, identifying the specific domains necessary for this interaction, suggesting a cooperative role in germline regulation. Importantly, the loss of otu produces similar defects to those observed in Sakura mutants, highlighting their functional collaboration.
The authors provide compelling evidence that Sakura is a critical regulator of germ cell fate, maintenance, and differentiation in Drosophila. This regulatory role is mediated through the modulation of pMad and Bam expression. However, the phenotypes observed in the germarium appear to stem from reduced pMad levels, which subsequently trigger premature and ectopic expression of Bam. This aberrant Bam expression could lead to increased CycA levels and altered transcriptional regulation, impacting piRNA expression. Given Sakura's role in pMad expression, it would be insightful to investigate whether overexpression of Mad or pMad could mitigate these phenotypic defects (UAS-Mad line is available at Bloomington Drosophila Stock Center).
As suggested reviewer 1, we tested whether overexpression of Mad could rescue or mitigate the loss of sakura phenotypic defects, by using nos-Gal4-VP16 > UASp-Mad-GFP in the background of sakura<sup>null</sup>. As shown in Fig S11, we did not observe any mitigation of defects.
Then, we also tested whether expressing a constitutive active form of Tkv, by using UAS-Dcr2, NGT-Gal4 > UASp-tkv.Q235D in the background of sakura<sup>RNAi</sup>. As shown in Fig S12, we did not observe any mitigation of defects by this approach either.
A major concern is the overstated role of Sakura in regulating Orb. The data does not reveal mislocalized Orb; rather, a mislocalized oocyte and cytoskeletal breakdown, which may be secondary consequences of defects in oocyte polarity and structure rather than direct misregulation of Orb. The conclusion that Sakura is necessary for Orb localization is not supported by the data. Orb still localizes to the oocyte until about stage 6. In the later stage, it looks like the cytoskeleton is broken down and the oocyte is not positioned properly, however, there is still Orb localization in the ~8-stage egg chamber in the oocyte. This phenotype points towards a defect in the transport of Orb and possibly all other factors that need to localize to the oocyte due to cytoskeletal breakdown, not Orb regulation directly. While this result is very interesting it needs further evaluation on the underlying mechanism. For example, the decrease in E-cadherin levels leads to a similar phenotype and Bam is known to regulate E-cadherin expression. Is Bam expressed in these later knockdowns?
We examined Bam and DE-Cadherin expression in later RNAi knockdowns driven by ToskGal4. As shown in Fig S9, Bam was not expressed in these later knockdowns compared with controls. DE-Cadherin staining suggested a disorganized structure in late-stage egg chambers.
We agree that we overstated a role of Sakura in regulating Orb in the initial manuscript. We changed the text to avoid overstating.
The manuscript would benefit from a more balanced interpretation of the data concerning Sakura's role in Orb regulation. Furthermore, a more expanded discussion on Sakura's potential role in pMad regulation is needed. For example, since Otu and Bam are involved in translational regulation, do the authors think that Mad is not translated and therefore it is the reason for less pMad? Currently the discussion presents just a summary of the results and not an extension of possible interpretation discussed in context of present literature.
We changed the text to avoid overstating a role of Sakura in regulating Orb localization.
Based on our newly added results showing that transgenic overexpression of Mad could not rescue or mitigate the phenotypic defects of sakura<sup>null</sup> mutant (Fig S11), we do not think the reason for less pMad is less translation of Mad.
Reviewer #3 (Public review):
In this very thorough study, the authors characterize the function of a novel Drosophila gene, which they name Sakura. They start with the observation that sakura expression is predicted to be highly enriched in the ovary and they generate an anti-sakura antibody, a line with a GFP-tagged sakura transgene, and a sakura null allele to investigate sakura localization and function directly. They confirm the prediction that it is primarily expressed in the ovary and, specifically, that it is expressed in germ cells, and find that about 2/3 of the mutants lack germ cells completely and the remaining have tumorous ovaries. Further investigation reveals that Sakura is required for piRNA-mediated repression of transposons in germ cells. They also find evidence that sakura is important for germ cell specification during development and germline stem cell maintenance during adulthood. However, despite the role of sakura in maintaining germline stem cells, they find that sakura mutant germ cells also fail to differentiate properly such that mutant germline stem cell clones have an increased number of "GSC-like" cells. They attribute this phenotype to a failure in the repression of Bam by dpp signaling. Lastly, they demonstrate that sakura physically interacts with otu and that sakura and otu mutants have similar germ cell phenotypes. Overall, this study helps to advance the field by providing a characterization of a novel gene that is required for oogenesis. The data are generally high-quality and the new lines and reagents they generated will be useful for the field. However, there are some weaknesses and I would recommend that they address the comments in the Recommendations for the authors section below.
Recommendations for the authors:
Reviewer #1 (Recommendations for the authors):
General Comments:
(1) The gene nomenclature: As mentioned in the text, Sakura means cherry blossom and is one of the national flowers of Japan. I am not sure whether the phenotype of the CG14545 mutant is related to Sakura or not. I would like to suggest the authors reconsider the naming.
The striking phenotype of sakura mutant is tumorous and germless ovarioles. The tumorous phenotype, exhibiting lots of round fusome in germarium visualized by anti-Hts staining, looks like cherry blossom blooming to us. Also, the germless phenotype reminds us falling of the cherry blossom, especially considering that the ratio of tumorous phenotype decreases and that of germless decreases over fly age. Furthermore, “Sakura” symbolizes birth and renewal in Japanese culture (the last author of this manuscript is Japanese). Our findings indicated that the gene sakura is involved in regulation of renewal and differentiation of GSCs (which leads to birth). These are the reasons for the naming, which we would like to keep.
(2) In many of the microscopic photographs in the figures, especially for the merged confocal images, the resolution looks low, and the images appear blurred, making it difficult to judge the authors' claims. Also, the Alpha Fold structure in Figure 10A requires higher contrast images. The magnification of the images is often inadequate (e.g. Figures 3A, 3B, 5E, 7A, etc). The authors should take high-magnification images separately for the germarium and several different stages of the egg chambers and lay out the figures.
We are very sorry for the low-resolution images. This was caused when the original PDF file with high-resolution images was compressed in order to meet the small file size limit in the eLife submission portal. In the revised submission, we used high-resolution images.
Specific Comments
(1) How Sakura can cooperate with Otu remains unanswered. Sakura does not regulate deubiquitinase activity in vitro. Both sakura and otu appear to be involved in the Dpp-Smad signaling pathway and in the spatial control of Bam expression in the germarium, whereas Otu has been reported to act in concert with Bam to deubiquitinate and stabilize Cyc A for proper cystoblast differentiation. Therefore, it is plausible that the stabilization of Cyc A in the Sakura mutant is an indirect consequence of Bam misexpression and independent of the Sakura-Otu interaction. The authors may need to provide much deeper insight into the mechanism by which Sakura plays roles in these seemingly separable steps to orchestrate germ cell maintenance and differentiation during early oogenesis.
Yes, it is possible that the stabilization of CycA in the sakura mutant is an indirect consequence of Bam misexpression and independent of the Sakura-Otu interaction. To test the significance and role of the Sakura-Otu interaction, we have attempted to identify Sakura point mutants that lose interaction with Otu. If such point mutants were successfully obtained, we were planning to test if their transgene expression could rescue the phenotypes of sakura mutant as the wild-type transgene did. However, after designing and testing the interaction of over 30 point mutants with Otu, we could not obtain such mutant version of Sakura yet. We will continue making efforts, but it is beyond the scope of the current study. We hope to address this important point in future studies.
(2) Figure 3A and Figure 4: The authors show that piRNA production is abolished in Sakura KO ovaries. It is known that piRNA amplification (the ping-pong cycle) occurs in the Vasa-positive perinuclear nuage in nurse cells. Is the nuage normally formed in the absence of Sakura? The authors provide high-magnification images in the germarium expressing Vas-GFP. How does Sakura, and possibly Out, contribute to piRNA production? Are the defects a direct or indirect consequence of the loss of Sakura?
We provided higher magnification images of germarium expressing Vasa-EGFP in sakura mutant background (Fig 3A and 3B). The nuage formation does not seem to be dysregulated in sakura mutant. Currently, we do not know if the piRNA defects are direct or indirect consequence of the loss of Sakura. This question cannot be answered easily. We hope to address this in future studies.
(3) Figure 7 and Figure 12: The authors showed that Dpp-Smad signaling was abolished in Sakura KO germline cells. The same defects were also observed in otu mutant ovaries (Figure 12B). How does the Sakura-Otu axis contribute to the Dpp-Smad pathway in the germline?
As we mentioned in the response to comment (1), we attempted to test the significance and role of the Sakura-Otu interaction, including in the Dpp-Smad pathway in the germline, but we have not yet been able to obtain loss-of-interaction mutant(s) of Sakura. We hope to address this in future studies.
(4) Figure 9 and Fig 10: The authors raised antibodies against both Sakura and Otu, but their specificities were not provided. For Western blot data, the authors should provide whole gel images as source data files. Also, the authors argue that the Otu band they observed corresponds to the 98-kDa isoform (lines 302-304). The molecular weight on the Western blot alone would be insufficient to support this argument.
When we submitted the initial manuscript, we also submitted original, uncropped, and unmodified whole Western blot images for all gel images to the eLife journal, as requested. We did the same for this revised submission. I believe eLife makes all those files available for downloading to readers.
In the newly added Fig S13B, we used very young 2-5 hours ovaries and 3-7 days ovaries. 2-5 days ovaries contain only mostly pre-differentiated germ cells. Older ovaries (3-7 days in our case here) contain all 14 stages of oogenesis and later stages predominate in whole ovary lysates.
As reported in previous literature (Sass et al. 1995), we detected a higher abundance of the 104 kDa Otu isoform than the 98 kDa isoform in from 2-5 hours ovaries and predominantly the 98 kDa isoform in 3-7 days ovaries (Fig S13B). These results confirmed that the major Otu isoform we detected in Western blot, all of which uses old ovaries except for the 2-5 hours ovaries in Fig S13B, is the 98 kDa isoform.
(5) Otu has been reported to regulate ovo and Sxl in the female germline. Is Sakura involved in their regulation?
We examined sxl alternative splicing pattern in sakura mutant ovaries. As shown in Fig S6, we detected the male-specific isoform of sxl RNA and a reduced level of the female-specific sxl isoform in sakura mutant ovaries. Thus Sakura seems to be involved in sxl splicing in the female germline, while further studies will be needed to understand whether Sakura has a direct or indirect role here.
(6) Lines 443-447: The GSC loss phenotype in piwi mutant ovaries is thought to occur in a somatic cell-autonomous manner: both piwi-mutant germline clones and germline-specific piwi knockdown do not show the GSC-loss phenotype. In contrast, the authors provide compelling evidence that Sakura functions in the germline. Therefore, the Piwi-mediated GSC maintenance pathway is likely to be independent of the Sakura-Otu axis.
We changed the text accordingly.
Reviewer #2 (Recommendations for the authors):
Overall, this is a cleanly written manuscript, with some sentences/sections that are confusing the way they are constructed (i.e. Line 37-38, 334, section on Flp/FRT experiments).
We rewrote those sections to avoid confusion.
Comment for all merged image data: the quality of the merged images is very poor - the individual channels are better but should also be reprocessed for more resolved image data sets. Also, it would be helpful to have boundaries drawn in an individual panel to identify the regions of the germarium, as cartooned in Figure S1A (which should be brought into Figure 1) F-actin or Vsg staining would have helped throughout the manuscript to enhance the visualization of described phenotypes.
We are very sorry for the low-resolution images. This was caused when the original PDF file with high-resolution images was compressed in order to meet the small file size limit in the eLife submission portal. In the revised submission, we used high-resolution images.
We outlined the germarium in Fig 1E.
We brought the former FigS1 into Fig 1A.
We provided Phalloidin (F-Actin) staining images in Fig S7.
All p-values seem off. I recommend running the data through the student t-test again.
We used the student t-test to calculate p-values and confirmed that they are correct. We don’t understand why the reviewer thinks all p-values seem off.
In the original manuscript, as we mentioned in each figure legends, we used asterisk (*) to indicate p-value <0.05, without distinguishing whether it’s <0.001, <0.01< or <0.05.
Probably reviewer 2 is suggesting us to use ***, **, and *, to indicate p-value of <0.001, <0.01, and <0.05, respectively? If so, we now followed reviewer2’s suggestions.
Figure 1
(1) Within the text, C is mentioned before A.
We updated the text and now we mentioned Fig 1A before Fig 1C.
(2) B should be the supplemental figure.
We moved the former Fig 1B to Supplemental Figure 1.
(3) C - How were the different egg chamber stages selected in the WB? Naming them 'oocytes' is deceiving. Recommend labeling them as 'egg chambers', since an oocyte is claimed to be just the one-cell of that cyst.
We changed the labeling to egg chambers.
(4) Is the antibody not detecting Sakura in IF? There is no mention of this anywhere in the manuscript.
While our Sakura antibody detects Sakura in IF, it seems to detect some other proteins as well. Since we have Sakura-EGFP fly strain (which fully rescues sakura<sup>null</sup> phenotypes) to examine Sakura expression and localization without such non-specific signal issues, we relied on Sakura-EGFP rather than anti-Sakura antibodies for IF.
(5) Expand on the reliance of the sakura-EGFP fly line. Does this overexpression cause any phenotypes?
sakura-EGFP does not cause any phenotypes in the background of sakura[+/+] and sakura[+/-].
(6) Line 95 "as shown below" is not clear that it's referencing panel D.
We now referenced Fig 1D.
(7) Re: Figures 1 E and F. There is no mention of Hts or Vasa proteins in the text.<br /> "Sakura-EGFP was not expressed in somatic cells such as terminal filament, cap cells, escort cells, or follicle cells (Figure 1E). In the egg chamber, Sakura-EGFP was detected in the cytoplasm of nurse cells and was enriched in developing oocytes (Figure 1F)". Outline these areas or label these structures/sites in the images. The color of Merge labels is confusing as the blue is not easily seen.
We mentioned Hts and Vasa in the text. We labeled the structures/sites in the images and updated the color labeling.
Figure 2
(1) Entire figure is not essential to be a main figure, but rather supplemental.
We don’t agree with the reviewer. We think that the female fertility assay data, where sakura null mutant exhibits strikingly strong phenotype, which was completely rescued by our Sakura-EGFP transgene, is very important data and we would like to present them in a main figure.
(2) 2A- one star (*) significance does not seem correct for the presented values between 0 and 100+.
In the original manuscript, as we mentioned in each figure legends, we used asterisk (*) to indicate p-value <0.05, without distinguishing whether it’s <0.001, <0.01< or <0.05.
Probably reviewer 2 is suggesting us to use ***, **, and *, to indicate p-value of <0.001, <0.01, and <0.05, respectively? If so, we now followed reviewer2’s suggestions.
(3) 2C images are extremely low quality. Should be presented as bigger panels.
We are very sorry for the low-resolution images. This was caused when the original PDF file with high-resolution images was compressed in order to meet the small file size limit in the eLife submission portal. In the revised submission, we used high-resolution images. We also presented as bigger panels.
Figure 3
(1) "We observed that some sakura<sup>null</sup> /null ovarioles were devoid of germ cells ("germless"), while others retained germ cells (Fig 3A)" What is described is, that it is hard to see. Must have a zoomed-in panel.
We provided zoomed-in panels in Fig 3B
(2) C - The control doesn't seem to match. Must zoom in.
We provided matched control and also zoomed in.
(3) For clarity, separate the tumorous and germless images.
In the new image, only one tumorous and one germless ovarioles are shown with clear labeling and outline, for clarity.
(4) Use arrows to help clearly indicate the changes that occur. As they are presented, they are difficult to see.
We updated all the panels to enhance clarity.
(5) Line 158 seems like a strong statement since it could be indirect.
We softened the statement.
Figure 4
(1) Line 188-189 - Conclusion is an overstatement.
We softened the statement.
(2) Is the piRNA reduction due to a change in transcription? Or a direct effect by Sakura?
We do not know the answers to these questions. We hope to address these in future studies.
Figure 5
(1) D - It might make more sense if this graph showed % instead of the numbers.
We did not understand the reviewer’s point. We think using numbers, not %, makes more sense.
(2) Line 213 - explain why RNAi 2 was chosen when RNAi 1 looks stronger.
Fly stock of RNAi line 2 is much healthier than RNAi line 1 (without being driven Gal4) for some reasons. We had a concern that the RNAi line 1 might contain an unwanted genetic background. We chose to use the RNAi 2 line to avoid such an issue.
(3) In Line 218 there's an extra parenthesis after the PGC acronym.
We corrected the error.
(4) TOsk-Gal4 fly is not in the Methods section.
We mentioned TOsk-Gal4 in the Methods.
Figure 6:
(1) The FLP-FRT section must be rewritten.
We rewrote the FLP-FRT section.
(2) A - include statistics.
We included statistics using the chi-square test.
(3) B - is not recalled in the Results text.
We referred Fig 6B in the text.
(4) Line 232 references Figure 3, but not a specific panel.
We referred Fig 3A, 3C, 3D, and 3E, in the text.
Figure 7/8 - can go to Supplemental.
We moved Fig 8 to supplemental. However, we think Fig 7 data is important and therefore we would like to present them as a main figure.
(1) There should be CycA expression in the control during the first 4 divisions.
Yes, there is CycA expression observed in the control during the first 4 divisions, while it’s much weaker than in sakura<sup>null</sup> clone.
(2) Helpful to add the dotted lines to delineate (A) as well.
We added a dotted outline for germarium in Fig 7A.
(3) Line 263 CycA is miswritten as CyA.
We corrected the typo.
Figure 9
(1) Otu antibody control?
We validated Otu antibody in newly added Fig 10C and Fig S13A.
(2) Which Sakura-EGFP line was used? sakura het. or null background? This isn't mentioned in the text, nor legend.
We used Sakura-EGFP in the background of sakura[+/+]. We added this information in the methods and figure legend.
(3) C - Why the switch to S2 cells? Not able to use the Otu antibody in the IP of ovaries?
We can use the Otu antibody in the IP of ovaries. However, in anti-Sakura Western after anti-Otu IP, antibody light chain bands of the Otu antibodies overlap with the Sakura band. Therefore, we switched to S2 cells to avoid this issue by using an epitope tag.
Figure 10
(1) A- The resolution of images of the ribbon protein structure is poor.
We are very sorry for the low-resolution images. This was caused when the original PDF file with high-resolution images was compressed in order to meet the small file size limit in the eLife submission portal. In the revised submission, we used high-resolution images.
(2) A table summarizing the interactions between domains would help bring clarity to the data presented.
We added a table summarizing the fragment interaction results.
(3) Some images would be nice here to show that the truncations no longer colocalize.
We did not understand the reviewer’s points. In our study, even for the full-length proteins.
We have not shown any colocalization of Sakura and Otu in S2 cells or in ovaries, except that they both are enriched in developing oocytes in egg chambers.
Figure 12
(1) A - control and RNAi lines do not match.
We provided matched images.
(2) In general, since for Sakura, only its binding to Otu was identified and since they phenocopy each other, doesn't most of the characterization of Sakura just look at Otu phenotypes? Does Sakura knockdown affect Otu localization or expression level (and vice versa)?
We tested this by Western (Fig S15) and IF (Fig 12). Sakura knockdown did not decrease Otu protein level, and Otu knockdown did not decrease Sakura protein level (Fig S15). In sakura<sup>null</sup> clone, Otu level was not notably affected (Fig 12). In sakura<sup>null</sup> clone, Otu lost its localization to the posterior position within egg chambers.
Figure S6
(1) It is Luciferase, not Lucifarase.
We corrected the typo.
Reviewer #3 (Recommendations for the authors):
(1) It is interesting that germless and tumorous phenotypes coexist in the same population of flies. Additional consideration of these essentially opposite phenotypes would significantly strengthen the study. For example, do they co-exist within the same fly and are the tumorous ovarioles present in newly eclosed flies or do they develop with age? The data in Figure 8 show that bam knockdown partially suppresses the germless phenotype. What effect does it have on the tumorous phenotype? Is transposon expression involved in either phenotype? Do Sakura mutant germline stem cell clones overgrow relative to wild-type cells in the same ovariole? Does sakura RNAi driven by NGT-Gal4 only cause germless ovaries or does it also cause tumorous phenotypes? What happens if the knockdown of Sakura is restricted to adulthood with a Gal80ts? It may not be necessary to answer all of these questions, but more insight into how these two phenotypes can be caused by loss of sakura would be helpful.
We performed new experiments to answer these questions.
do they co-exist within the same fly and are the tumorous ovarioles present in newly eclosed flies or do they develop with age?
Tumorous and germless ovarioles coexist in the same fly (in the same ovary). Tumorous ovarioles are present in very young (0-1 day old) flies, including newly eclosed (Fig S5). The ratio of germless ovarioles increases and that of tumorous ovarioles decreases with age (Fig S5).
The data in Figure 8 show that bam knockdown partially suppresses the germless phenotype. What effect does it have on the tumorous phenotype?
bam knockdown effect on tumorous phenotype is shown in Fig S10. bam knockdown increased the ratio of tumorous ovarioles and the number of GSC-like cells.
Is transposon expression involved in either phenotype?
Since our transposon-piRNA reporter uses germline-specific nos promoter, it is expressed only in germ line cells, so we cannot examine in germless ovarioles.
Do Sakura mutant germline stem cell clones overgrow relative to wild-type cells in the same ovariole?
Yes, Sakura mutant GSC clones overgrow. Please compare Fig 6C and Fig S8.
Does sakura RNAi driven by NGT-Gal4 only cause germless ovaries or does it also cause tumorous phenotypes?
Fig S10 and Fig S12 show the ovariole phenotypes of sakura RNAi driven by NGT-Gal4. It causes both germless and tumorous phenotypes.
What happens if the knockdown of Sakura is restricted to adulthood with a Gal80ts?
Our mosaic clone was induced at the adult stage, so we already have data of adulthood-specific loss of function. Gal80ts does not work well with nos-Gal4.
(2) The idea that the excessive bam expression in tumorous ovaries is due to a failure of bam repression by dpp signaling is not well-supported by the data. Dpp signaling is activated in a very narrow region immediately adjacent to the niche but the images in Figure 7A show bam expression in cells that are very far away from the niche. Thus, it seems more likely to be due to a failure to turn bam expression off at the 16-cell stage than to a failure to keep it off in the niche region. To determine whether bam repression in the niche region is impaired, it would be important to examine cells adjacent to the niche directly at a higher magnification than is shown in Figure 7A.
We provided higher magnification images of cells adjacent to the niche in new Fig 7A.
We found that cells adjacent to the niche also express Bam-GFP.
That said, we agree with the reviewer. A failure to turn bam expression off at the 16-cell stage may be an additional or even a main cause of bam misexpression in sakura mutant. We added this in the Discussion.
(3) In addition, several minor comments should be addressed:
a. Does anti-Sakura work for immunofluorescence?
While our Sakura antibody detects Sakura in IF, it seems to detect some other proteins as well. Since we have Sakura-EGFP fly strain to examine Sakura expression and localization without such non-specific signal issues, we relied on Sakura-EGFP rather than anti-Sakura antibodies.
b. Please provide insets to show the phenotypes indicated by the different color stars in Figure 3C more clearly.
We provided new, higher-magnification images to show the phenotypes more clearly.
c. Please indicate the frequency of the expression patterns shown in Figure 4D (do all ovarioles in each genotype show those patterns or is there variable penetrance?).
We indicated the frequency.
d. An image showing TOskGal4 driving a fluorophore should be provided so that readers can see which cells express Gal4 with this driver combination.
It has been already done in the paper ElMaghraby et al, GENETICS, 2022, 220(1), iyab179, so we did not repeat the same experiment.
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Author response:
The following is the authors’ response to the original reviews
Public Reviews:
Reviewer #1 (Public review):
Contractile Injection Systems (CIS) are versatile machines that can form pores in membranes or deliver effectors. They can act extra or intracellularly. When intracellular they are positioned to face the exterior of the cell and hence should be anchored to the cell envelope. The authors previously reported the characterization of a CIS in Streptomyces coelicolor, including significant information on the architecture of the apparatus. However, how the tubular structure is attached to the envelope was not investigated. Here they provide a wealth of evidence to demonstrate that a specific gene within the CIS gene cluster, cisA, encodes a membrane protein that anchors the CIS to the envelope. More specifically, they show that:
- CisA is not required for assembly of the structure but is important for proper contraction and CIS-mediated cell death
- CisA is associated to the membrane (fluorescence microscopy, cell fractionation) through a transmembrane segment (lacZ-phoA topology fusions in E. coli)
- Structural prediction of interaction between CisA and a CIS baseplate component<br /> - In addition they provide a high-resolution model structure of the >750-polypeptide Streptomyces CIS in its extended conformation, revealing new details of this fascinating machine, notably in the baseplate and cap complexes.
All the experiments are well controlled including trans-complemented of all tested phenotypes.
One important information we miss is the oligomeric state of CisA.
Thank you for this suggestion. We now provide information on the potential oligomeric state of CisA. We performed further AlphaFold3 modelling of CisA using an increasing number of CisA protomers (1 to 8). We ran predictions for the configuration using the sequence of the well-folded C-terminal CisA domain (amino acids 285-468), which includes the transmembrane domain and the conserved domain that shares similarities to carbohydrate-degrading domains. The obtained confidence scores (mean values for pTM=0.73, ipTM=0.7, n=5) indicate that CisA can assemble into a pentamer and that this oligomerization is mediated through the interaction of the C-terminal solute-binding like superfamily domain.
We have added this information to the revised manuscript (Fig. 3b/c) and further discuss the possible implications of CisA oligomerization for its proposed mode of action.
While it would have been great to test the interaction between CisA and Cis11, to perform cryo-electron microscopy assays of detergent-extracted CIS structures to maintain the interaction with CisA, I believe that the toxicity of CisA upon overexpression or upon expression in E. coli render these studies difficult and will require a significant amount of time and optimization to be performed. It is worth mentioning that this study is of significant novelty in the CIS field because, except for Type VI secretion systems, very few membrane proteins or complexes responsible for CIS attachment have been identified and studied.
We thank this reviewer for their highly supportive and positive comments on our manuscript and we are grateful for their recognition of the novelty of our study, particularly in the context of membrane proteins and complexes involved in CIS attachment.
We agree that further experimental evidence on direct interaction between CisA and Cis11 would have strengthened our model on CisA function. However, as noted by this reviewer, this additional work is technically challenging and currently beyond the scope of this study.
Reviewer #2 (Public review):
Summary:
The overall question that is addressed in this study is how the S. coelicolor contractile injection system (CISSc) works and affects both cell viability and differentiation, which it has been implicated to do in previous work from this group and others. The CISSc system has been enigmatic in the sense that it is free-floating in the cytoplasm in an extended form and is seen in contracted conformation (i.e. after having been triggered) mainly in dead and partially lysed cells, suggesting involvement in some kind of regulated cell death. So, how do the structure and function of the CISSc system compare to those of related CIS from other bacteria, does it interact with the cytoplasmic membrane, how does it do that, and is the membrane interaction involved in the suggested role in stress-induced, regulated cell death? The authors address these questions by investigating the role of a membrane protein, CisA, that is encoded by a gene in the CIS gene cluster in S. coelicolor. Further, they analyse the structure of the assembled CISSc, purified from the cytoplasm of S. coelicolor, using single-particle cryo-electron microscopy.
Strengths:
The beautiful visualisation of the CIS system both by cryo-electron tomography of intact bacterial cells and by single-particle electron microscopy of purified CIS assemblies are clearly the strengths of the paper, both in terms of methods and results. Further, the paper provides genetic evidence that the membrane protein CisA is required for the contraction of the CISSc assemblies that are seen in partially lysed or ghost cells of the wild type. The conclusion that CisA is a transmembrane protein and the inferred membrane topology are well supported by experimental data. The cryo-EM data suggest that CisA is not a stable part of the extended form of the CISSc assemblies. These findings raise the question of what CisA does.
We thank Reviewer #2 for the overall positive evaluation of our manuscript and the constructive criticism.
Weaknesses:
The investigations of the role of CisA in function, membrane interaction, and triggering of contraction of CIS assemblies, are important parts of the paper and are highlighted in the title. However, the experimental data provided to answer these questions appear partially incomplete and not as conclusive as one would expect.
We acknowledge that some aspects of our work remain unanswered. We are currently unable to conduct additional experiments because the two leading postdoctoral researchers on this project have moved on to new positions. We currently don’t have the extra manpower with a similar skill set to pick up the project.
The stress-induced loss of viability is only monitored with one method: an in vivo assay where cytoplasmic sfGFP signal is compared to FM5-95 membrane stain. Addition of a sublethal level of nisin lead to loss of sfGFP signal in individual hyphae in the WT, but not in the cisA mutant (similarly to what was previously reported for a CIS-negative mutant). Technically, this experiment and the example images that are shown give rise to some concern. Only individual hyphal fragments are shown that do not look like healthy and growing S. coelicolor hyphae. Under the stated growth conditions, S. coelicolor strains would normally have grown as dense hyphal pellets. It is therefore surprising that only these unbranched hyphal fragments are shown in Fig. 4ab.
We thank this Reviewer for their thoughtful criticism regarding the viability assays and the data presented in Figure 4. We acknowledge the importance of ensuring that the presented images reflect the physiological state of S. coelicolor under the stated growth conditions and recognize that hyphal fragments shown in Figure 4 do not fully capture the typical morphology of S. coelicolor. As pointed out by this reviewer, S. coelicolor grows in large hyphal clumps when cultured in liquid media, making the quantification of fluorescence intensities in hyphae expressing cytoplasmic GFP or stained with the membrane dye FM5-95 particularly challenging. To improve the image analysis and quantification of GFP and FM5-95-fluorescent intensities across the three S. coelicolor strains (wildtype, cisA deletion mutant and the complemented cisA mutant), we vortexed the cell samples before imaging to break up hyphal clumps, increasing hyphal fragments. The hyphae shown in our images were selected as representative examples across three biological replicates.
Further, S. coelicolor would likely be in a stationary phase when grown 48 h in the rich medium that is stated, giving rise to concern about the physiological state of the hyphae that were used for the viability assay. It would be valuable to know whether actively growing mycelium is affected in the same way by the nisin treatment, and also whether the cell death effect could be detected by other methods.
The reasoning behind growing S. coelicolor for 48 h before performing the fluorescence-based viability assay was that we (DOI: 10.1038/s41564-023-01341-x ) and others (e.g.: DOI: 10.1038/s41467-023-37087-7 ) previously showed that the levels of CIS particles peak at the transition from vegetative to reproductive/stationary growth, thus indicating that CIS activity is highest during this growth stage. The obtained results in this manuscript are consistent with previous results, in which we showed a similar effect on the viability of wildtype versus cis-deficient S. coelicolor strains (DOI: 10.1038/s41564-023-01341-x ) using nisin, the protonophore CCCP and UV radiation. The results presented in this study and our previous study are based on biological triplicate experiments and appropriate controls. Furthermore, our results are in agreement with the findings reported in a complementary study by Vladimirov et al. (DOI: 10.1038/s41467-023-37087-7 ) that used a different approach (SYTO9/PI staining of hyphal pellets) to demonstrate that CIS-deficient mutants exhibit decreased hyphal death.
Taken together, we believe that the results obtained from our fluorescence-based viability assay provide strong experimental evidence that functional CIS mediate hyphal cell death in response to exogenous stress.
The model presented in Fig. 5 suggests that stress leads to a CisA-dependent attachment of CIS assemblies to the cytoplasmic membrane, and then triggering of contraction, leading to cell death. This model makes testable predictions that have not been challenged experimentally. Given that sublethal doses of nisin seem to trigger cell death, there appear to be possibilities to monitor whether activation of the system (via CisA?) indeed leads to at least temporally increased interaction of CIS with the membrane.
We thank this reviewer for their suggestions on how to test our model further. This is a challenging experiment because we do not know the exact dynamics of how nisin stress is perceived and transmitted to CisA and CIS particles.
In an attempt to address this point, we have performed co-immunoprecipitation experiments using S. coelicolor cells that produced CisA-FLAG as bait, and which were treated with a sub-lethal nisin concentration for 0/15/45 min. Mass spectrometry analysis of co-eluted peptides did not show the presence of CIS-associated peptides at the analyzed timepoints. While we cannot exclude the possibility that our experimental assay requires further optimization to successfully demonstrate a CisA-CIS interaction (e.g. optimization of the use of detergents to improve the solubilization of CisA from Streptomyces membrane, which is currently not an established method), an alternative and equally valid hypothesis is that the interaction between CIS particles and CisA is transient and therefore difficult to capture. We would like to mention, however, that we did detect CisA peptides in crude purifications of CIS particles from nisin-stressed cells (Supplementary Table 2, manuscript: line 301/302), supporting our proposed model that CisA can associate with CIS particles in vivo.
Further, would not the model predict that stress leads to an increased number of contracted CIS assemblies in the cytoplasm? No clear difference in length of the isolated assemblies if Fig. S7 is seen between untreated and nisin-exposed cells, and also no difference between assemblies from WT and cisA mutant hyphae.
The reviewer is correct that there is no clear difference in length in the isolated CIS particles shown in Figure S7. This is in line with our results, which show that CisA is not required for the correct assembly of CIS particles and their ability to contract in the presence and absence of nisin treatment. The purpose of Figure S7 was to support this statement. We would like to note that the particles shown in Figure S7 were purified from cell lysates using a crude sheath preparation protocol, during which CIS particles generally contract irrespective of the presence or absence of CisA. Thus, we cannot comment on whether there is an increased number of contracted CIS assemblies in the cytoplasm of nisin-exposed cells. To answer this point, we would need to acquire additional cryo-electron tomograms (cyroET) of the different strains treated with nisin. CryoET is an extremely time and labor-intensive task and given that we currently don’t know the exact dynamics of the CIS-CisA interaction following exogenous stress, we believe this experiment is beyond the scope of this work.
The interaction of CisA with the CIS assembly is critical for the model but is only supported by Alphafold modelling, predicting interaction between cytoplasmic parts of CisA and Cis11 protein in the baseplate wedge. An experimental demonstration of this interaction would have strengthened the conclusions.
We agree that direct experimental evidence of this interaction would have further strengthened the conclusions of our study, and we have extensively tried to provide additional experimental evidence. Unfortunately, because of the toxicity of cisA expression in E. coli and the possibly transient nature of the interaction under the experimental conditions used, we were unable to confirm this interaction by biochemical or biophysical techniques, such as co-purification or bacterial two-hybrid assays. Despite these technical challenges, we believe that the AlphaFold predictions provided a valuable hypothesis about the role of CisA in firing and the function of CIS particles in S. coelicolor.
The cisA mutant showed a similarly accelerated sporulation as was previously reported for CIS-negative strains, which supports the conclusion that CisA is required for function of CISSc. But the results do not add any new insights into how CIS/CisA affects the progression of the developmental life cycle and whether this effect has anything to do with the regulated cell death that is caused by CIS. The same applies to the effect on secondary metabolite production, with no further mechanistic insights added, except reporting similar effects of CIS and CisA inactivations.
Thank you for your feedback on this aspect of the manuscript. We would like to note that the main focus of this study was to provide further insight into how CIS contraction and firing are mediated in Streptomyces. We used the analysis of accelerated sporulation and secondary metabolite production as a readout to directly assess the functionality of CIS in the presence or absence of CisA and to complement the in situ cryoET data. In summary, our data significantly expand our knowledge of CIS function and firing in Streptomyces and suggest a model in which CisA plays an essential role in mediating the interaction of CIS particles with the membrane, which is required for CIS-mediated cell death. We discuss this model in more detail in the revised manuscript (Line 274-283).
We agree that we still don’t fully understand the full nature of the signals that trigger CIS contraction, but we do know that the production of CIS is an integral part of the Streptomyces multicellular life cycle as demonstrated by two independent previous studies by us and others (DOI: 10.1038/s41564-023-01341-x and DOI: 10.1038/s41467-023-37087-7 ).
We further speculate that the assembly and CisA-dependent firing of Streptomyces CIS particles could present a molecular mechanism to dismantle part of the vegetative mycelium. This form of “regulated cell death” could provide two key benefits: (1) to prevent the spread of local cellular damage to the rest of mycelium and (2) to provide additional nutrients for the rest of the mycelium to delay the terminal differentiation into spores, which in turn also affects the production of secondary metabolites.
Concluding remarks:
The work will be of interest to anyone interested in contractile injection systems, T6SS, or similar machineries, as well for people working on the biology of streptomycetes. There is also a potential impact of the work in the understanding of how such molecular machineries could have been co-opted during evolution to become a mechanism for regulated cell death. However, this latter aspect remains still poorly understood. Even though this paper adds excellent new structural insights and identifies a putative membrane anchor, it remains elusive how the Streptomyces CIS may lead to cell death. It is also unclear what the advantage would be to trigger death of hyphal compartments in response to stress, as well as how such cell death may impact (or accelerate) the developmental progression. Finally, it is inescapable to wonder whether the Streptomyces CIS could have any role in protection against phage infection.
We thank Reviewer #2 for the overall supportive assessment of our work. We will briefly discuss functional CIS's impact on Streptomyces development in the revised manuscript. We previously tested if Streptomyces could defend against phages but have not found any experimental evidence to support this idea (unpublished data). The analysis of phage defense mechanisms is an underdeveloped area in Streptomyces research, partly due to the currently limited availability of a diverse phage panel.
Reviewer #3 (Public review):
Summary:
In this work, Casu et al. have reported the characterization of a previously uncharacterized membrane protein CisA encoded in a non-canonical contractile injection system of Streptomyces coelicolor, CISSc, which is a cytosolic CISs significantly distinct from both intracellular membrane-anchored T6SSs and extracellular CISs. The authors have presented the first high-resolution structure of extended CISSc structure. It revealed important structural insights in this conformational state. To further explore how CISSc interacted with cytoplasmic membrane, they further set out to investigate CisA that was previously hypothesized to be the membrane adaptor. However, the structure revealed that it was not associated with CISSc. Using fluorescence microscope and cell fractionation assay, the authors verified that CisA is indeed a membrane-associated protein. They further determined experimentally that CisA had a cytosolic N-terminal domain and a periplasmic C-terminus. The functional analysis of cisA mutant revealed that it is not required for CISSc assembly but is essential for the contraction, as a result, the deletion significantly affects CISSc-mediated cell death upon stress, timely differentiation, as well as secondary metabolite production. Although the work did not resolve the mechanistic detail how CisA interacts with CISSc structure, it provides solid data and a strong foundation for future investigation toward understanding the mechanism of CISSc contraction, and potentially, the relation between the membrane association of CISSc, the sheath contraction and the cell death.
Strengths:
The paper is well-structured, and the conclusion of the study is supported by solid data and careful data interpretation was presented. The authors provided strong evidence on (1) the high-resolution structure of extended CISSc determined by cryo-EM, and the subsequent comparison with known eCIS structures, which sheds light on both its similarity and different features from other subtypes of eCISs in detail; (2) the topological features of CisA using fluorescence microscopic analysis, cell fractionation and PhoA-LacZα reporter assays, (3) functions of CisA in CISSc-mediated cell death and secondary metabolite production, likely via the regulation of sheath contraction.
Weaknesses:
(1) The data presented are not sufficient to provide mechanistic details of CisA-mediated CISSc contraction, as authors are not able to experimentally demonstrate the direct interaction between CisA with baseplate complex of CISSc (hypothesized to be via Cis11 by structural modeling), since they could not express cisA in E. coli due to its potential toxicity. Therefore, there is a lack of biochemical analysis of direct interaction between CisA and baseplate wedge. In addition, there is no direct evidence showing that CisA is responsible for tethering CISSc to the membrane upon stress, and the spatial and temporal relation between membrane association and contraction remains unclear. Further investigation will be needed to address these questions in future.
We thank Reviewer #3 for the supportive evaluation and constructive feedback of our study in the non-public review. We appreciate the recognition of the technical limitations of experimentally demonstrating a direct interaction between CisA and CIS baseplate complex, and we agree that further investigations in the future will hopefully provide a full mechanistic understanding of the spatiotemporal interaction of CisA and CIS particular and the subsequent CIS firing.
To further improve the manuscript, we will revise the text and clarify figures and figure legends as suggested in the non-public review.
Discussion:
Overall, the work provides a valuable contribution to our understanding on the structure of a much less understood subtype of CISs, which is unique compared to both membrane-anchored T6SSs and host-membrane targeting eCISs. Importantly, the work serves as a good foundation to further investigate how the sheath contraction works here. The work contributes to expanding our understanding of the diverse CIS superfamilies.
Thank you.
Recommendations for the authors:
Reviewer #1 (Recommendations for the authors):
- Magnification of the potential CisA-Cis11 model, with side chains at the interface, should be shown in Supplementary Figures 9/10 to help the reader appreciates the intercation between the two subunits.
Done. A zoomed-in view of the relevant side chains at the CisA-Cis11 interface has been added to Supplementary Figure 9e. For clarity, we decided not to highlight these residues in Supplementary Figure 10 because they are identical to those in Figure 9e.
- A model where CisA is positionned onto the baseplate (by merging the CisA-Cis11 model and the baseplate structure) will also be informative for the reader.
We agree that such a presentation would be helpful to visualize the proposed CisA-Cis11 interaction. However, the Cis11 residues predicted to bind CisA are buried in our cryoEM single-particle structure of the elongated Streptomyces CIS. This is not surprising, as the structure is based on a previously established non-contractile CIS mutant variant (PMCID: PMC10066040), which means we were only able to capture one specific configuration of the baseplate complex in the current work. This baseplate configuration is most likely structurally distinct from the baseplate configuration in contracted CIS particles. A similar observation was also reported for the baseplate complex of eCIS particles from Algoriphagus machipongonesis (PMCID: PMC8894135 ).
We speculate that in Streptomyces, initial non-specific contacts between CisA and cytoplasmic CIS particles induce a rearrangement of baseplate components, resulting in the exposure of the relevant Cis11 residues, which in turn facilitates a transient interaction between CisA and Cis11. This interaction then leads to additional conformational changes within the baseplate complex, triggering sheath contraction and CIS firing.
We believe that a transient binding step is a crucial part of the activation process, contributing to the dynamic nature of the system.
- Providing information on the oligomeric state of CisA will strenghten the manuscript. Authors may consider having blue-native gel analysis of CisA-3xFLAG extracted from Streptomyces or E. coli membranes, or in vivo chemical cross-linking coupled to SDS-PAGE analyses. In case these quite straightforward experiments are not possible, the authors may consider providing AF3 models of various CisA multimers.
Thank you for these suggestions. Unfortunately, we currently don’t have the capability to conduct additional experiments. However, we have performed additional AF3 modelling to explore potential different configurations of CisA. The results of these analyses suggest that CisA can assemble into a pentamer (see also Response to reviewer 1). We speculate that CisA may exist in different oligomeric states and that membrane-localized CisA monomers oligomerize into a larger protein complex in response to a cellular or extracellular (e.g. nisin) signal, which could then directly or indirectly interact with CIS particles in the cytoplasm to facilitate their recruitment to the membrane and CIS firing. Such a stress-dependent conformational change of CisA could also be a safety mechanism to prevent accidental interaction of CisA with CIS particles and CIS firing.
We now show the AF model for the predicted CisA pentamer in Figure 3b/c and discuss the potential implications of the different CisA configurations in the revised manuscript.
Reviewer #2 (Recommendations for the authors):
- The quantification of contracted versus extended CIS assemblies in the cytoplasm is only presented for the tomograms from the cisA mutant (graph in Fig. S2d). However, there are no data for the WT and complemented mutant to compare with. It would help to add such data, or at least refer to the previous quantification done for the WT in the previous paper. Further, would it be possible to illustrate the difference by measuring lengths of CIS assemblies and plot length distributions (assuming the extended ones are long and contracted are short)?
Thank you for your suggestions. We have included the results from our previous quantification of CIS assembly states observed in the WT in the revised manuscript (lines 106–110).
In the acquired tomograms of CIS particles observed in intact and dead hyphae, we consistently observed only two CIS conformations: the fully extended state (average length of 233 nm, diameter of 18 nm) and the fully contracted state (average length of 124 nm, diameter of 23 nm). We have added this information to the revised manuscript (lines 112-114).
- The Western blot in Fig. 3d, top panel, contains additional bands that are not mentioned. Are they non-specific bands? Absent in disA mutant? It would help if it was clarified in the legend what they are.
Correct, these additional bands are unspecific bands, which are also visible in the lysate and soluble fraction of wild-type sample (negative control, no FLAG-tagged protein). We have now labelled these bands in the figure and clarified the figure legend.
- Fig. S8a needs improvement. It was not possible to clearly see the stated effect of disA deletion on secondary metabolite production in these photos.
We agree and have removed figure panel S8a from the manuscript. The quantification of total actinorhodin production shown in Figure S8b convincingly shows a significantly reduction of actinorhodin production in the cisA deletion mutant compared to the wildtype and the complement mutant.
- It is not an important point, but the paragraph in lines 109-116 appears more like a re-iteration of the Introduction than Results.
We agree. We have removed the highlighted text from the Results section and added some of the information to the introduction.
- Line 206 appears to have a typo. Should it not be WT instead of WT cisA?
Correct. This is a typo which has been fixed. Thank you.
- At the end of the Discussion, it is suggested that a stepwise mechanism of recruiting CIS to the membrane and then triggering firing would prevent unwanted activation and self-inflicted death. Since both steps appear to be dependent in DisA, it would be good to more clearly spell out how such a stepwise mechanism would work and how it could prevent spontaneous and erroneous firing of the system.
Thank you for this suggestion. We have revised the text to clarify the proposed stepwise mechanism. Based on additional structural modeling, we propose that the conserved extra-cytoplasmic domain of CisA may play a role in sensing stress signals. Binding of a ‘stress-associated molecule’ could induce a conformational change in CisA, a hypothesis supported by: (1) Foldseek protein structure searches, which suggest that the conserved C-terminal CisA domain resembles substrate/solute-binding proteins, and (2) AlphaFold3 models predicting that CisA can form a pentamer via its putative substrate-binding domain. This suggests that a transition from CisA monomers to pentamers in response to stress may serve as a key checkpoint, activating CisA and facilitating the recruitment of CIS assemblies to the membrane, either directly or indirectly. Conversely, in the absence of a stress signal, CisA is likely to remain in its monomeric (resting) form, incapable of triggering CIS firing. We have revised the discussion to explain the proposed model in more detail.
We recognize that this model poses many testable hypotheses that we currently cannot test but aim to address in the future.
Reviewer #3 (Recommendations for the authors):
There are a few concerns potentially worth addressing to strengthen the study or for future investigation.
(1) It would be worth considering moving the first part of the result ('CisA is required for CISSc contraction in situ') after presenting the structure of extended CISSc, and combining it with the last part of the result section ('CisA is essential for the cellular function of CISSc'), as both parts describe the functional characterization of CisA.
We appreciate the reviewer’s suggestion but have chosen to retain the current order of the results. As this manuscript focuses on the role of CisA, we believe that first establishing a functional link between CisA and CIS contraction provides essential context and motivation for the study.
(2) Line 169: it is not clear to me if the fusion of CisA with mCherry is functional (if it complements the native CisA). Moreover, it was not shown if its localization changes under nisin stress or in the strain with non-contractile CISSc.
We have not tested if the CisA-mCherry fusion is fully functional. While we cannot exclude the possibility that the activity of this protein fusion is compromised in vivo, we believe that the described accumulation of CisA-mCherry at the membrane is accurate. This conclusion is further supported by the results obtained from protein fractionation experiments and the membrane topology assay (Figure 3).
We did not examine if the localization of CisA-mCherry changes in CIS mutant strains under nisin-stress, but this is something we will follow up on in the future.
(3) In ref 18, the previous work from the same team presented a functional fluorescent fusion of Cis2 (sheath), thus, it will be interesting to see if (i) Cis2 localization and dynamics is affected by the absence of CisA under normal and stressed conditions; (ii) if Cis2 shows any co-localization with CisA under normal and especially stressed conditions, and potentially, its timing correlation to ghost cell formation by time-lapse imaging of both fusions.
We thank this reviewer for the suggestions, and we plan to address these questions in the future.
(4) Line 261: it was hypothesized by authors that the cytosolic portion of CisA was required for interacting with Cis11. While it was not possible to verify the direct interaction at current state, a S. coelicolor mutant lacking this cytosolic domain may be of help to indirectly test the hypothesis. Moreover, it would be interesting to see if the cytosolic region alone is enough to induce the contraction upon stress (by removing the TM-C region). If so, whether it leads to cell death, or if it is insufficient to cause cell death without membrane association despite the sheath contraction. If not, it would suggest that membrane association occurs before contraction.
These are really great suggestions and if we had the manpower and resources, we would have performed these experiments. We plan to follow up on these questions in the future.
However, additional structural modelling of CisA indicates that CisA may exist in different configurations (see response to Reviewer #1 and #2), a monomeric and/or a pentameric configuration. In these structural models (revised Figure 3), CisA oligomerization is mediated by the annotated periplasmic solute-binding domain. It is conceivable that CisA oligomerization (e.g. in response to a stress signal) presents a critical checkpoint that results in a conformational change within CisA monomers that subsequently drives CisA oligomerization into a configuration primed to interact with CIS particles. We would therefore speculate that the expression of just the cytoplasmic CisA domain may not be sufficient for CIS contraction and cell death.
(5) Line 263: as it was not possible to express full-length cisA in E. coli, making it difficult to assess the interaction between CisA and Cis11, it may be worth considering expressing the cytosolic portion of CisA (ΔTM-C) instead of full-length CisA, or alternatively performing a co-immunoprecipitation assay of CisA (i.e., with an affinity tag) from S. coelicolor cultures under stressed conditions. However, I am aware that these may be beyond the scope of this work but can be considered for future investigation in general.
Thank you for your suggestions and your understanding that some of this work is beyond the scope of this work. We have performed CisA-FLAG co-immunoprecipitation experiments from S. coelicolor cultures that were treated with nisin for 0/15/45 min. However, mass spectrometry analysis of co-eluted peptides did not show the presence of CIS-associated peptides at the analysed timepoints. While we cannot exclude technical issues with our assays that resulted in an inefficient solubilization of CisA from Streptomyces membranes, an alternative hypothesis is that the interaction between CIS particles and CisA is very transient and therefore difficult to capture. We would like to mention, however, that we did detect CisA peptides in crude purifications of CIS particles from nisin-stressed cells (Supplementary Table 2, manuscript: line 301/302), supporting our proposed model that CisA can associate with CIS particles in vivo.
Minor points:
(1) I will suggest moving Supplementary Fig 2d with control quantification of WT strain and complementation strain (similar to Fig 3g from ref 18) to the main Fig 1, as the quantitative representation with better comparison without going back and forth to ref 18.
Thank you for your suggestion. Instead of moving Supplementary Fig. 2d to the main figure, we have added additional information in lines 106–110 to discuss the previous quantification of CIS assembly states in the WT, as described in our earlier work. We believe this approach allows readers to easily reference our established quantification without compromising the flow of the main figures.
(2) Line 52/785: as work of Ref 12 has recently been published DOI: 10.1126/sciadv.adp7088, the reference should be updated accordingly.
This reference has been updated. Thank you.
(3) A brief description of key differences between contracted (ref 18) and extended sheath structure will be a good addition for a broader audience.
Thank you for this suggestion. We have added more information on lines 178–180.
(4) Fig 3d: it is not clear how well the samples from different fractions were normalized in amount (volume and cell density), but there was an inconsistency in the amount of CisA-Flag in lysate, vs. soluble and membrane fractions (total protein amount combined from soluble fraction and membrane fraction together seemed to be more than in the lysate, while in theory it should be more or less equal; and the amount of WhiA from WT seemed to be less than from the CisA-Flag strain). In the method section, it was mentioned that 'The final pellet was dissolved in 1/10 of the initial volume with wash buffer (no urea). Equi-volume amounts of fractions were mixed with 2x SDS sample buffer and analyzed by immunoblotting.' But it is still not clear whether equivalent amounts (normalized to the same OD for example) were used and if we could directly compare. A brief clarification in the legend of how samples were prepared is needed.
The samples were normalized by first using the same volume of starting material (similar culture density and incubation period for each strain) and by loading equal volumes of each fraction for analysis. After fractionation, equi-volume amounts of the soluble and membrane protein fractions were mixed with 2× SDS sample buffer and subjected to immunoblotting, ensuring a consistent basis for comparison between samples. We have revised the figure legend and Material and Method sections to make this clear.
We agree that the amount of CisA-3xFLAG appears slightly lower in the “Lysate” fraction compared to the “Membrane” fraction in Figure 3d (now Fig. 3f). However, this does not affect the overall conclusion of this experiment, showing that CisA-3xFLAG is clearly enriched in the membrane fraction.
For reference, please find below the uncropped version of this Western blot image. Based on the signal of the unspecific bands, we would like to argue that equal amounts of samples obtained from the WT control strain (no FLAG epitope present) and a strain producing CisA-3xFLAG were loaded for each of the fractions. When we revisited this data, we noted that the protein size marker was wrong. This has been fixed.
Author response image 1.
(5) Fig. 4f: statistical analysis is missing.
The missing statistical analysis has been added to this figure and figure legend.
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Author response:
(1) General Statements
As you will see in our attached rebuttal to the reviewers, we have added several new experiments and revised manuscript to fully address their concerns.
(2) Point-by-point description of the revisions
Reviewer #1:
Evidence, reproducibility and clarity
Summary:
The manuscript by Yang et al. describes a new CME accessory protein. CCDC32 has been previously suggested to interact with AP2 and in the present work the authors confirm this interaction and show that it is a bona fide CME regulator. In agreement with its interaction with AP2, CCDC32 recruitment to CCPs mirrors the accumulation of clathrin. Knockdown of CCDC32 reduces the amount of productive CCPs, suggestive of a stabilisation role in early clathrin assemblies. Immunoprecipitation experiments mapped the interaction of CCDC42 to the α-appendage of the AP2 complex α-subunit. Finally, the authors show that the CCDC32 nonsense mutations found in patients with cardio-facial-neuro-developmental syndrome disrupt the interaction of this protein to the AP2 complex. The manuscript is well written and the conclusions regarding the role of CCDC32 in CME are supported by good quality data. As detailed below, a few improvements/clarifications are needed to reinforce some of the conclusions, especially the ones regarding CFNDS.
We thank the referee for their positive comments. In light of a recently published paper describing CCDC32 as a co-chaperone required for AP2 assembly (Wan et al., PNAS, 2024, see reviewer 2), we have added several additional experiments to address all concerns and consequently gained further insight into CCDC32-AP2 interactions and the important dual role of CCDC32 in regulating CME.
Major comments:
(1) Why did the protein could just be visualized at CCPs after knockdown of the endogenous protein? This is highly unusual, especially on stable cell lines. Could this be that the tag is interfering with the expressed protein function rendering it incapable of outcompeting the endogenous? Does this points to a regulated recruitment?
The reviewer is correct, this would be unusual; however, it is not the case. We misspoke in the text (although the figure legend was correct) these experiments were performed without siRNA knockdown and we can indeed detect eGFP-CCDC32 being recruited to CCPs in the presence of endogenous protein. Nonetheless, we repeated the experiment to be certain (see Author response image 1).
Author response image 1.
Cohort-averaged fluorescence intensity traces of CCPs (marked with mRuby-CLCa) and CCP-enriched eGFPCCDC32(FL).
(2) The disease mutation used in the paper does not correspond to the truncation found in patients. The authors use an 1-54 truncation, but the patients described in Harel et al. have frame shifts at the positions 19 (Thr19Tyrfs*12) and 64 (Glu64Glyfs*12), while the patient described in Abdalla et al. have the deletion of two introns, leading to a frameshift around amino acid 90. Moreover, to be precisely test the function of these disease mutations, one would need to add the extra amino acids generated by the frame shift. For example, as denoted in the mutation description in Harel et al., the frameshift at position 19 changes the Threonine 19 to a Tyrosine and ads a run of 12 extra amino acids (Thr19Tyrfs*12).
The label of the disease mutant p.(Thr19Tyrfs12) and p.(Glu64Glyfs12) is based on a 194aa polypeptide version of CCDC32 initiated at a nonconventional start site that contains a 9 aa peptide (VRGSCLRFQ) upstream of the N-terminus we show. Thus, we are indeed using the appropriate mutation site (see: https://www.uniprot.org/uniprotkb/Q9BV29/entry). The reviewer is correct that we have not included the extra 12 aa in our construct; however as these residues are not present in the other CFNDS mutants, we think it unlikely that they contribute to the disease phenotype. Rather, as neither of the clinically observed mutations contain the 78-98 aa sequence required for AP2 binding and CME function, we are confident that this defect contributed to the disease. Thus, we are including the data on the CCDC32(1-54) mutant, as we believe these results provide a valuable physiological context to our studies.
(3) The frameshift caused by the CFNDS mutations (especially the one studied) will likely lead to nonsense mediated RNA decay (NMD). The frameshift is well within the rules where NMD generally kicks in. Therefore, I am unsure about the functional insights of expressing a diseaserelated protein which is likely not present in patients.
We thank the reviewer for bringing up this concern. However, as shown in new Figure S1, the mutant protein is expressed at comparable levels as the WT, suggesting that NMD is not occurring.
(4) Coiled coils generally form stable dimers. The typically hydrophobic core of these structures is not suitable for transient interactions. This complicates the interpretation of the results regarding the role of this region as the place where the interaction to AP2 occurs. If the coiled coil holds a stable CCDC32 dimer, disrupting this dimer could reduce the affinity to AP2 (by reduced avidity) to the actual binding site. A construct with an orthogonal dimeriser or a pulldown of the delta78-98 protein with of the GST AP2a-AD could be a good way to sort this issue.
We were unable to model a stable dimer (or other oligomer) of this protein with high confidence using Alphafold 3.0. Moreover, we were unable to detect endogenous CCDC32 coimmunoprecipitating with eGFP-CCDC32 (Fig. S6C). Thus, we believe that the moniker, based solely on the alpha-helical content of the protein is a misnomer. We have explained this in the main text.
Minor comments:
(1) The authors interchangeably use the term "flat CCPs" and "flat clathrin lattices". While these are indeed related, flat clathrin lattices have been also used to refer to "clathrin plaques". To avoid confusion, I suggest sticking to the term "flat CCPs" to refer to the CCPs which are in their early stages of maturation.
Agreed. Thank you for the suggestion. We have renamed these structures flat clathrin assemblies, as they do not acquire the curvature needed to classify them as pits, and do not grow to the size that would classify then as plaques.
Significance
General assessment:
CME drives the internalisation of hundreds of receptors and surface proteins in practically all tissues, making it an essential process for various physiological processes. This versatility comes at the cost of a large number of molecular players and regulators. To understand this complexity, unravelling all the components of this process is vital. The manuscript by Yang et al. gives an important contribution to this effort as it describes a new CME regulator, CCDC32, which acts directly at the main CME adaptor AP2. The link to disease is interesting, but the authors need to refine their experiments. The requirement for endogenous knockdown for recruitment of the tagged CCDC32 is unusual and requires further exploration.
Advance:
The increased frequency of abortive events presented by CCDC32 knockdown cells is very interesting, as it hints to an active mechanism that regulates the stabilisation and growth of clathrin coated pits. The exact way clathrin coated pits are stabilised is still an open question in the field.
Audience:
This is a basic research manuscript. However, given the essential role of CME in physiology and the growing number of CME players involved in disease, this manuscript can reach broader audiences.
We thank the referee for recognizing the ‘interesting’ advances our studies have made and for considering these studies as ‘an important contribution’ to ‘an essential process for various physiological processes’ and able ‘to reach broader audiences’. We have addressed and reconciled the reviewer’s concerns in our revised manuscript.
Field of expertise of the reviewer:
Clathrin mediated endocytosis, cell biology, microscopy, biochemistry.
Reviewer #2:
Evidence, reproducibility and clarity
In this manuscript, the authors demonstrate that CCDC32 regulates clathrin-mediated endocytosis (CME). Some of the findings are consistent with a recent report by Wan et al. (2024 PNAS), such as the observation that CCDC32 depletion reduces transferrin uptake and diminishes the formation of clathrin-coated pits. The primary function of CCDC32 is to regulate AP2 assembly, and its depletion leads to AP2 degradation. However, this study did not examine AP2 expression levels. CCDC32 may bind to the appendage domain of AP2 alpha, but it also binds to the core domain of AP2 alpha.
We thank the reviewer for drawing our attention to the Wan et al. paper, that appeared while this work was under review. However, our in vivo data are not fully consistent with the report from Wan et al. The discrepancies reveal a dual function of CCDC32 in CME that was masked by complete knockout vs siRNA knockdown of the protein, and also likely affected by the position of the GFP-tag (C- vs N-terminal) on this small protein. Thus:
- Contrary to Wan et al., we do not detect any loss of AP2 expression (see new Figure S3A-B) upon siRNA knockdown. Most likely the ~40% residual CCDC32 present after siRNA knockdown is sufficient to fulfill its catalytic chaperone function but not its structural role in regulating CME beyond the AP2 assembly step.
- Contrary to Wan et al., we have shown that CCDC32 indeed interacts with intact AP2 complex (Figure S3C and 6B,C) showing that all 4 subunits of the AP2 complex co-IP with full length eGFP-CCDC32. Interestingly, whereas the full length CCDC32 pulls down the intact AP2 complex, co-IP of the ∆78-98 mutant retains its ability to pull down the β2-µ2 hemicomplex, its interactions with α:σ2 are severely reduced. While this result is consistent with the report of Wan et al that CCDC32 binds to the α:σ2 hemi-complex, it also suggests that the interactions between CCDC32 and AP2 are more complex and will require further studies.
- Contrary to Wan et al., we provide strong evidence that CCDC32 is recruited to CCPs. Interestingly, modeling with AlphaFold 3.0 identifies a highly probably interaction between alpha helices encoded by residues 66-91 on CCDC32 and residues 418-438 on α. The latter are masked by µ2-C in the closed confirmation of the AP2 core, but exposed in the open confirmation triggered by cargo binding, suggesting that CCDC32 might only bind to membrane-bound AP2.
Thus, our findings are indeed novel and indicate striking multifunctional roles for CCDC32 in CME, making the protein well worth further study.
(1) Besides its role in AP2 assembly, CCDC32 may potentially have another function on the membrane. However, there is no direct evidence showing that CCDC32 associates with the plasma membrane.
We disagree, our data clearly shows that CCDC32 is recruited to CCPs (Fig. 1B) and that CCPs that fail to recruit CCDC32 are short-lived and likely abortive (Fig. 1C). Wan et al. did not observe any colocalization of C-terminally tagged CCDC32 to CCPs, whereas we detect recruitment of our N-terminally tagged construct, which we also show is functional (Fig. 6F). Further, we have demonstrated the importance of the C-terminal region of CCDC32 in membrane association (see new Fig. S7). Thus, we speculate that a C-terminally tagged CCDC32 might not be fully functional. Indeed, SIM images of the C-terminally-tagged CCDC32 in Wan et al., show large (~100 nm) structures in the cytosol, which may reflect aggregation.
(2) CCDC32 binds to multiple regions on AP2, including the core domain. It is important to distinguish the functional roles of these different binding sites.
We have localized the AP2-ear binding region to residues 78-99 and shown these to be critical for the functions we have identified. As described above we now include data that are complementary to those of Wan et al. However, our data also clearly points to additional binding modalities. We agree that it will be important and map these additional interactions and identify their functional roles, but this is beyond the scope of this paper.
(3) AP2 expression levels should be examined in CCDC32 depleted cells. If AP2 is gone, it is not surprising that clathrin-coated pits are defective.
Agreed and we have confirmed this by western blotting (Figure S3A-B) and detect no reduction in levels of any of the AP2 subunits in CCDC32 siRNA knockdown cells. As stated above this could be due to residual CCDC32 present in the siRNA KD vs the CRISPR-mediated gene KO.
(4) If the authors aim to establish a secondary function for CCDC32, they need to thoroughly discuss the known chaperone function of CCDC32 and consider whether and how CCDC32 regulates a downstream step in CME.
Agreed. We have described the Wan et al paper, which came out while our manuscript was in review, in our Introduction. As described above, there are areas of agreement and of discrepancies, which are thoroughly documented and discussed throughout the revised manuscript.
(5) The quality of Figure 1A is very low, making it difficult to assess the localization and quantify the data.
The low signal:noise in Fig. 1A the reviewer is concerned about is due to a diffuse distribution of CCDC32 on the inner surface of the plasma membrane. We now, more explicitly describe this binding, which we believe reflects a specific interaction mediated by the C-terminus of CCDC32; thus the degree of diffuse membrane binding we observe follows: eGFP-CCDC32(FL)> eGFPCCDC32(∆78-98)>eGFP-CCDC32(1-54)~eGFP/background (see new Fig. S7). Importantly, the colocalization of CCDC32 at CCPs is confirmed by the dynamic imaging of CCPs (Fig 1B).
(6) In Figure 6, why aren't AP2 mu and sigma subunits shown?
Agreed. Not being aware of CCDC32’s possible dual role as a chaperone, we had assumed that the AP2 complex was intact. We have now added this data in Figure 6 B,C and Fig. S3C, as discussed above.
Page 5, top, this sentence is confusing: "their surface area (~17 x 10 nm<sup>2</sup>) remains significantly less than that required for the average 100 nm diameter CCV (~3.2 x 103 nm<sup>2</sup>)."
Thank you for the criticism. We have clarified the sentence and corrected a typo, which would definitely be confusing. The section now reads, “While the flat CCSs we detected in CCDC32 knockdown cells were significantly larger than in control cells (Fig. 4D, mean diameter of 147 nm vs. 127 nm, respectively), they are much smaller than typical long-lived flat clathrin lattices (d≥300 nm)(Grove et al., 2014). Indeed, the surface area of the flat CCSs that accumulate in CCDC32 KD cells (mean ~1.69 x 10<sup>4</sup> nm<sup>2</sup>) remains significantly less than the surface area of an average 100 nm diameter CCV (~3.14 x 10<sup>4</sup> nm<sup>2</sup>). Thus, we refer to these structures as ‘flat clathrin assemblies’ because they are neither curved ‘pits’ nor large ‘lattices’. Rather, the flat clathrin assemblies represent early, likely defective, intermediates in CCP formation.”
Significance
Overall, while this work presents some interesting ideas, it remains unclear whether CCDC32 regulates AP2 beyond the assembly step.
Our responses above argue that we have indeed established that CCDC32 regulates AP2 beyond the assembly step. We have also identified several discrepancies between our findings and those reported by Wan et al., most notably binding between CCDC32 and mature AP2 complexes and the AP2-dependent recruitment of CCDC32 to CCPs. It is possible that these discrepancies may be due to the position of the GFP tag (ours is N-terminal, theirs is C-terminal; we show that the N-terminal tagged CCDC32 rescues the knockdown phenotype, while Wan et al., do not provide evidence for functionality of the C-terminal construct).
Reviewer #3:
Evidence, reproducibility and clarity (Required):
In this manuscript, Yang et al. characterize the endocytic accessory protein CCDC32, which has implications in cardio-facio-neuro-developmental syndrome (CFNDS). The authors clearly demonstrate that the protein CCDC32 has a role in the early stages of endocytosis, mainly through the interaction with the major endocytic adaptor protein AP2, and they identify regions taking part in this recognition. Through live cell fluorescence imaging and electron microscopy of endocytic pits, the authors characterize the lifetimes of endocytic sites, the formation rate of endocytic sites and pits and the invagination depth, in addition to transferrin receptor (TfnR) uptake experiments. Binding between CCDC32 and CCDC32 mutants to the AP2 alpha appendage domain is assessed by pull down experiments. Together, these experiments allow deriving a phenotype of CCDC32 knock-down and CCDC32 mutants within endocytosis, which is a very robust system, in which defects are not so easily detected. A mutation of CCDC32, known to play a role in CFNDS, is also addressed in this study and shown to have endocytic defects.
We thank the reviewer for their positive remarks regarding the quality of our data and the strength of our conclusions.
In summary, the authors present a strong combination of techniques, assessing the impact of CCDC32 in clathrin mediated endocytosis and its binding to AP2, whereby the following major and minor points remain to be addressed:
- The authors show that CCDC32 depletion leads to the formation of brighter and static clathrin coated structures (Figure 2), but that these were only prevalent to 7.8% and masked the 'normal' dynamic CCPs. At the same time, the authors show that the absence of CCDC32 induces pits with shorter life times (Figure 1 and Figure 2), the 'majority' of the pits.
Clarification is needed as to how the authors arrive at these conclusions and these numbers. The authors should also provide (and visualize) the corresponding statistics. The same statement is made again later on in the manuscript, where the authors explain their electron microscopy data. Was the number derived from there?
These points are critical to understanding CCDC32's role in endocytosis and is key to understanding the model presented in Figure 8. The numbers of how many pits accumulate in flat lattices versus normal endocytosis progression and the actual time scales could be included in this model and would make the figure much stronger.
Thank you for these comments. We understand the paradox between the visual impression and the reality of our dynamic measurements. We have been visually misled by this in previous work (Chen et al., 2020), which emphasizes the importance of unbiased image analysis afforded to us through the well-documented cmeAnalysis pipeline, developed by us (Aguet et al., 2013) and now used by many others (e.g. (He et al., 2020)).
The % of static structures was not derived from electron microscopy data, but quantified using cmeAnalysis, which automatedly provides the lifetime distribution of CCPs. We have now clarified this in the manuscript and added a histogram (Fig. S4) quantifying the fraction of CCPs in lifetime cohorts <20s, 21-60s, 61-100s, 101-150s and >150s (static).
- In relation to the above point, the statistics of Figure 2E-G and the analysis leading there should also be explained in more detail: For example, what are the individual points in the plot (also in Figures 6G and 7G)? The authors should also use a few phrases to explain software they use, for example DASC, in the main text.
Each point in these bar graphs represents a movie, where n≥12. These details have been added to the respective figure legend. We have also added a brief description of DASC analysis in the text.
- There are several questions related to the knock-down experiments that need to be addressed:
Firstly, knock-down of CCDC32 does not seem to be very strong (Figure S2B). Can the level of knock-down be quantified?
We have now quantified the KD efficiency. It is ~60%. This turns out to be fortuitous (see responses to reviewer 2), as a recent publication, which came out after we completed our study, has shown by CRISPR-mediated knockout, that CCD32 also plays an essential chaperone function required for AP2 assembly. We do not see any reduction in AP2 levels or its complex formation under our conditions (see new Supplemental Figure S3), which suggests that the effects of CCDC32 on CCP dynamics are more sensitive to CCDC32 concentration than its roles as a chaperone. Our phenotypes would have been masked by more efficient depletion of CCDC32.
In page 6 it is indicated that the eGFP-CCDC32(1-54) and eGFP-CCDC32(∆78-98) constructs are siRNA-resistant. However in Fig S2B, these proteins do not show any signal in the western blot, so it is not clear if they are expressed or simply not detected by the antibody. The presence of these proteins after silencing endogenous CCDC32 needs to be confirmed to support Figures 6 and Figures 7, which critically rely on the presence of the CCDC32 mutants.
Unfortunately, the C-terminally truncated CCDC32 proteins are not detected because they lack the antibody epitope, indeed even the ∆78-98 deletion is poorly detected (compare the GFP blot in new S1A with the anti-CCDC32 blot in S1B). However, these constructs contain the same siRNA-resistance mutation as the full length protein. That they are expressed and siRNA resistant can be seen in Fig. S2A (now Fig. S1A) blotting for GFP.
In Figures 6 and 7, siRNA knock-down of CCDC32 is only indicated for sub-figures F to G. Is this really the case? If not, the authors should clarify. The siRNA knock-down in Figure 1 is also only mentioned in the text, not in the figure legend. The authors should pay attention to make their figure legends easy to understand and unambiguous.
No, it is not the case. Thank you for pointing out the uncertainty. We have added these details to the Figure legends and checked all Figure legends to ensure that they clearly describe the data shown.
- It is not exactly clear how the curves in Figure 3C (lower panel) on the invagination depth were obtained. Can the authors clarify this a bit more? For example, what are kT and kE in Figure 3A? What is I0? And how did the authors derive the logarithmic function used to quantify the invagination depth? In the main text, the authors say that the traces were 'logarithmically transformed'. This is not a technical term. The authors should refer to the actual equation used in the figure.
This analysis was developed by the Kirchhausen lab (Saffarian and Kirchhausen, 2008). We have added these details and reference them in the Figure legend and in the text. We also now use the more accurate descriptor ‘log-transformed’.
- In the discussion, the claim 'The resulting dysregulation of AP2 inhibits CME, which further results in the development of CFNDS.' is maybe a bit too strong of a statement. Firstly, because the authors show themselves that CME is perturbed, but by no means inhibited. Secondly, the molecular link to CFNDS remains unclear. Even though CCDC32 mutants seem to be responsible for CFNDS and one of the mutant has been shown in this study to have a defect in endocytosis and AP2 binding, a direct link between CCDC32's function in endocytosis and CFNDS remains elusive. The authors should thus provide a more balanced discussion on this topic.
We have modified and softened our conclusions, which now read that the phenotypes we see likely “contribute to” rather than “cause” the disease.
- In Figure S1, the authors annotate the presence of a coiled-coil domain, which they also use later on in the manuscript to generate mutations. Could the authors specify (and cite) where and how this coiled-coil domain has been identified? Is this predicted helix indeed a coiled-coil domain, or just a helix, as indicated by the authors in the discussion?
See response to Reviewer 1, point 4. We have changed this wording to alpha-helix. The ‘coiled-coil’ reference is historical and unlikely a true reflection of CCDC32 structure. AlphaFold 3.0 predictions were unable to identify with certainly any coiled-coil structures, even if we modelled potential dimers or trimers; and we find no evidence of dimerization of CCDC32 in vivo. We have clarified this in the text.
Minor comments
- In general, a more detailed explanation of the microscopy techniques used and the information they report would be beneficial to provide access to the article also to non-expert readers in the field. This concerns particularly the analysis methods used, for example:
How were the cohort-averaged fluorescence intensity and lifetime traces obtained?
How do the tools cmeAnalysis and DASC work? A brief explanation would be helpful.
We have expanded Methods to add these details, and also described them in the main text.
- The axis label of Figure 2B is not quite clear. What does 'TfnR uptake % of surface bound' mean? Maybe the authors could explain this in more detail in the figure legend? Is the drop in uptake efficiency also accessible by visual inspection of the images? It would be interesting to see that.
This is a standard measure of CME efficiency. 'TfnR uptake % of surface bound' = Internalized TfnR/Surface bound TfnR. Again, images may be misleading as defects in CME lead to increased levels of TfnR on the cell surface, which in turn would result in more Tfn uptake even if the rate of CME is decreased.
- Figure 4: How is the occupancy of CCPs in the plasma membrane measured? What are the criteria used to divide CCSs into Flat, Dome or Sphere categories?
We have expanded Methods to add these details. Based on the degree of invagination, the shapes of CCSs were classified as either: flat CCSs with no obvious invagination; dome-shaped CCSs that had a hemispherical or less invaginated shape with visible edges of the clathrin lattice; and spherical CCSs that had a round shape with the invisible edges of clathrin lattice in 2D projection images. In most cases, the shapes were obvious in 2D PREM images. In uncertain cases, the degree of CCS invagination was determined using images tilted at ±10–20 degrees. The area of CCSs were measured using ImageJ and used for the calculation of the CCS occupancy on the plasma membrane.
- Figure 5B: Can the authors explain, where exactly the GFP was engineered into AP2 alpha? This construct does not seem to be explained in the methods section.
We have added this information. The construct, which corresponds to an insertion of GFP into the flexible hinge region of AP2, at aa649, was first described by (Mino et al., 2020) and shown to be fully functional. This information has been added to the Methods section.
- Figure S1B: The authors should indicate the colour code used for the structural model.
We have expanded our structural modeling using AlphaFold 3.0 in light of the recent publication suggesting the CCDC32 interacts with the µ2 subunit and does not bind full length AP2. These results are described in the text. The color coding now reflects certainty values given by AlphaFold 3.0 (Fig. S6B, D).
- The list of primers referred to in the materials and methods section does not exist. There is a Table S1, but this contains different data. The actual Table S1 is not referenced in the main text. This should be done.
We apologize for this error. We have now added this information in Table S2.
Significance (Required):
In this study, the authors analyse a so-far poorly understood endocytic accessory protein, CCDC32, and its implication for endocytosis. The experimental tool set used, allowing to quantify CCP dynamics and invagination is clearly a strength of the article that allows assessing the impact of an accessory protein towards the endocytic uptake mechanism, which is normally very robust towards mutations. Only through this detailed analysis of endocytosis progression could the authors detect clear differences in the presence and absence of CCDC32 and its mutants. If the above points are successfully addressed, the study will provide very interesting and highly relevant work allowing a better understanding of the early phases in CME with implication for disease.
The study is thus of potential interest to an audience interested in CME, in disease and its molecular reasons, as well as for readers interested in intrinsically disordered proteins to a certain extent, claiming thus a relatively broad audience. The presented results may initiate further studies of the so-far poorly understood and less well known accessory protein CCDC32.
We thank the reviewer for their positive comments on the significance of our findings and the importance of our detailed phenotypic analysis made possible by quantitative live cell microscopy. We also believe that our new structural modeling of CCDC32 and our findings of complex and extensive interactions with AP2 make the reviewers point regarding intrinsically disordered proteins even more interesting and relevant to a broad audience. We trust that our revisions indeed address the reviewer’s concerns.
The field of expertise of the reviewer is structural biology, biochemistry and clathrin mediated endocytosis. Expertise in cell biology is rather superficial.
References:
Aguet, F., Costin N. Antonescu, M. Mettlen, Sandra L. Schmid, and G. Danuser. 2013. Advances in Analysis of Low Signal-to-Noise Images Link Dynamin and AP2 to the Functions of an Endocytic Checkpoint. Developmental Cell. 26:279-291.
Chen, Z., R.E. Mino, M. Mettlen, P. Michaely, M. Bhave, D.K. Reed, and S.L. Schmid. 2020. Wbox2: A clathrin terminal domain–derived peptide inhibitor of clathrin-mediated endocytosis. Journal of Cell Biology. 219.
Grove, J., D.J. Metcalf, A.E. Knight, S.T. Wavre-Shapton, T. Sun, E.D. Protonotarios, L.D. Griffin, J. Lippincott-Schwartz, and M. Marsh. 2014. Flat clathrin lattices: stable features of the plasma membrane. Mol Biol Cell. 25:3581-3594.
He, K., E. Song, S. Upadhyayula, S. Dang, R. Gaudin, W. Skillern, K. Bu, B.R. Capraro, I. Rapoport, I. Kusters, M. Ma, and T. Kirchhausen. 2020. Dynamics of Auxilin 1 and GAK in clathrinmediated traffic. J Cell Biol. 219.
Mino, R.E., Z. Chen, M. Mettlen, and S.L. Schmid. 2020. An internally eGFP-tagged α-adaptin is a fully functional and improved fiduciary marker for clathrin-coated pit dynamics. Traffic. 21:603-616.
Saffarian, S., and T. Kirchhausen. 2008. Differential evanescence nanometry: live-cell fluorescence measurements with 10-nm axial resolution on the plasma membrane. Biophys J. 94:23332342.
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Reply to the reviewers
Reviewer #1
Evidence, reproducibility and clarity
In their manuscript de las Mercedes Carro et al investigated the role of Ago proteins during spermatogenesis by producing a triple knockout of Ago 1, 3 and 4. They first describe the pattern of expression of each protein and of Ago2 during the differentiation of male germ cells, then they describe the spermatogenesis phenotype of triple knockout males, study gene deregulation by scRNA seq and identify novel interacting proteins by co-IP mass spectrometry, in particular BRG1/SMARCA4, a chromatin remodeling factor and ATF2 a transcription factor. The main message is that Ago3 and 4 are involved in the regulation of XY gene silencing during meiosis, and also in the control of autosomal gene expression during meiosis. Overall the manuscript is well written, the topic, very interesting and the experiments, well-executed. However, there are some parts of the methodology and data interpretation that are unclear (see below).
Major comments
1= Please clarify how the triple KO was obtained, and if it is constitutive or specific to the male germline. In the result section a Cre (which cre?) is mentioned but it is not mentioned in the M&M. On Figure S1, a MICER VECTOR is shown instead of a deletion, but nothing is explained in the text nor legend. Could the authors provide more details in the results section as well as in the M&M ? This is essential to fully interpret the results obtained for this KO line, and to compare its phenotype to other lines (such as lines 184-9 Comparison of triple KO phenotype with that of Ago4 KO). Also, if it is a constitutive KO, the authors should mention if they observed other phenotypes in triple KO mice since AGO proteins are not only expressed in the male germline.
Response: We apologize for omitting this vital information. We have now incorporated a more detailed description of how the Ago413 mutant was created in the results and M&M sections (line 120 and 686 respectively).
As mentioned in the manuscript, Ago4, Ago1 and Ago3 are widely expressed in mammalian somatic tissues. Mutations or deletions of these genes does not disrupt development; however, there is limited research on the impact of these mutations in mammalian models in vivo. In humans, mutations in Ago1 and Ago3 genes are associated with neurological disorders, autism and intellectual disability (Tokita, M.J.,et al. 2015- doi: 10.1038/ejhg.2014.202., Sakaguchi et al. 2019- doi: 10.1016/j.ejmg.2018.09.004, Schalk et al 2021- doi: 10.1136/jmedgenet-2021-107751). In mouse, global deletion of Ago1 and Ago3 simultaneously was shown to increase mice susceptibility to influenza virus through impaired inflammation responses (Van Stry et al 2012- doi.org/10.1128/jvi.05303-11). Studies performed in female Ago413 mutants (the same mutant line used herein) have shown that knockout mice present postnatal growth retardation with elevated circulating leukocytes (Guidi et al 2023- doi: 10.1016/j.celrep.2023.113515). Other studies of double conditional knockout of Ago1 and Ago3 in the skin associated the loss of these Argonautes with decreased weight of the offspring and severe skin morphogenesis defects (Wang et al 2012- doi: 10.1101/gad.182758.111). In our study, we did not observe major somatic or overt behavioral phenotypes, and we did not observe statistical differences in body weights of null males compared to WT as shown in figure below.
2= The paragraph corresponding to G2/M analysis is unclear to me. Why was this analysis performed? What does the heatmap show in Figure S4? What is G2/M score? (Fig 2D). Lines 219-220, do the authors mean that Pachytene cells are in a cell phase equivalent to G2/M? All this paragraph and associated figures require more explanation to clarify the method and interpretation.
__Response: __We have modified the methods to include more information about how the cell cycle scoring used in Figures 2D and S4 were calculated and will add more information regarding the interpretation of these figures.
3= I have concerns regarding Fig2G: to be convincing the analysis needs to be performed on several replicates, and, it is essential to compare tubules of the same stage - which does not seem to be the case. This does not appear to be the case. Besides, co (immunofluorescent) staining with markers of different cell types should be shown to demonstrate the earlier expression of some markers and their colocalization with markers of the earlier stages.
__Response: __We agree with the Reviewer. New images with staged tubules will be added to the analysis of Figure 2G.
4= one important question that I think the authors should discuss regarding their scRNAseq: clusters are defined using well characterized markers. But Ago triple KO appears to alter the timing of expression of genes... could this deregulation affects the interperetation of scRNAseq clusters and results?
__Response: __We thank the reviewer for this suggestion and agree that including this information is important. We expect that, at most, this dysregulation impacts the edges of these clusters slightly. Given that marker genes that have been used to define cell types in these data are consistently expressed between the knockout and wildtype mice (see Figure S4A), we do not think that the cells in these clusters have different identities, just dysregulated expression programs. We have added the relevant sentence to the discussion, and will include additional supplemental figure panels to document this point more comprehensively.
5= XY gene deregulation is mentioned throughout the result section but only X chromosome genes seem to have been investigated.... Even the gene content of the Y is highly repetitive, it would be very interesting to show the level of expression of Y single copy and Y multicopy genes in a figure 3 panel.
__Response: __We agree with the reviewer that including analysis of Y-linked genes is important. We will add a supplemental figure which includes the Y:Autosome ratio and differential expression analysis.
6= Can the authors elaborate on the observation that X gene upregulation is visible in the KO before MSCI; that is in lept/zygotene clusters (and in spermatogonia, if the difference visible in 3A is significant?)
Response: We do see that X gene expression is upregulated before pachynema. Previous scRNA-seq studies that have looked at MCSI have seen that silencing of genes on the X and Y chromosomes starts before the cell clusters that are defined as pachynema, though silencing is not fully completed until pachynema. We have clarified this point in the manuscript.
7 = miRNA analysis: could the authors indicate if X encoded miRNA were identified and found deregulated? Because Ago4 has been shown to lead to a downregulation of miRNA, among which many X encoded. It is therefore puzzling to see that the triple KO does not recapitulate this observation. Were the analyses performed differently in the present study and in Ago4 KO study?
__Response: __The analysis identifying downregulation of miRNA in the original Ago4 mutant analysis was conducted relative to total small RNA expression. Amongst those altered miRNA families in the Ago4 mutants, we demonstrated both upregulation and downregulation of miRNA. We agree that confirming a similar global downregulation of miRNA counts compared to other small RNAs is important. Therefore, in a revised manuscript, we will add this information to the miRNA analysis section, especially highlighting the X chromosome-associated miRNAs, as well as whether the ratios between other small RNA classes change.
8 = The last results paragraph would also benefit from some additional information. It is not clear why the authors focused on enhancers and did not investigate promoters (or maybe they were but it's unclear). Which regions (size and location from TSS) were investigated for motif enrichment analyses? To what correspond the "transcriptional regulatory regions previously identified using dREG" mentioned in the M&M? I understand it's based on a previous article, but more info in the present manuscript would be useful.
Response: We thank the reviewer for this suggestion. The regions that were used for motif enrichment will be included as a supplementary information in the fully revised manuscript. We have also clarified in the methods that these transcriptional regulatory regions were downloaded from GEO and obtained from previous ChRO-seq data (from GEO) analysis. These data are run through the dREG pipeline that identifies regions predicted to contain transcription start sites, which include promoters and enhancers.
Minor comments
1) In the introduction: The sentence "Ago1 is not expressed in the germline from the spermatogonia stage onwards allowing us to use this model to study the roles of Ago4 and Ago3 in spermatogenesis." is misleading because Ago1 is expressed at least in spermatogonia; It would be more precise to write "after spermatogonia stage" and rephrase the sentence. Otherwise it is surprising to see AGO1 protein in testis lysate and it is not in line with the scRNA seq shown in figure 2.
__Response: __We agree with the Reviewers suggestion and have edited the sentence on line 100. This sentence now reads "Ago1 is not expressed in the germline after the spermatogonia stage allowing us to use this model to study the roles of Ago4 and Ago3 in spermatogenesis".
2) Could the authors precise if AGO proteins are expressed in other tissues? In somatic testicular cells?
__Response: __Expression patterns of mammalian AGOs have been described in somatic and testicular tissues for the mouse by Gonzales-Gonzales et al (2008) by qPCR. They found that Ago2 is expressed in all the somatic tissues analyzed (brain, spleen, heart, muscle and lung) as well as the testis, with the highest expression in brain and lowest in heart. Ago1 is highly expressed in spleen compared to all the tissues analyzed, while Ago3 and Ago4 showed highest expression in testis and brain. Within somatic tissues of the testis, the four argonautes are expressed in Sertoli cells, however, Ago1,3 and 4 expression is very low compared to Ago2, with the latter showing a 10-fold higher transcript level. We have included a sentence with this information in the introduction in line 89.
3) Pattern of expression: How do the authors explain that AGO3 disappears at the diplotene stage and reappears in spermatids?
__Response: __ Single cell RNAseq data in the germline shows reduced transcript for Ago3 from the Pachytene stage onwards, suggesting minimal if any new transcription in round spermatids. We hypothesize that the AGO3 protein present in the round spermatid stage is cytoplasmic, presumably coming from the pool of AGO3 in the chromatoid body, a cytoplasmic structure with functional association with the nucleus in round spermatids (Kotaja et al, 2003 doi: 10.1073/pnas.05093331).
4) It would be useful to show the timing of expression of AGO 1 to 4 throughout spermatogenesis in the first paragraph of the article. Maybe the authors could present data from fig2B earlier?
Response: We understand the Reviewers concern, however, given that Ago expression throughout spermatogenesis was obtained from scRNA seq, we consider that this data should be presented after introducing the Ago413 knockout and the scRNA seq experiment. As Ago1-4 expression was also described in an earlier manuscript by Gonzales-Gonzales et al in the mouse male germline, and our data aligns with this report, we included a sentence about these previous findings in the earlier results section.
5) Line 190: please modify the sentence "reveal no differences in cellular architecture of the seminiferous tubules when compared to wild-type males" to " reveal no gross differences..." since even without quantification of the different cell types it is visible that KO seminiferous tubules are different from WT tubules.
__Response: __We agree with the reviewer, and we modified line 190 (now 173) as suggested. Grossly, seminiferous tubules from Ago413 null males contain the same cell types as in wild type tubules, including spermatozoa. However, our studies show that the number and quality of germ cells is compromised in knockouts, as shown by sperm counts and TUNEL staining.
6) TUNEL analysis: please stage the tubules to determine the stage(s) at which apoptosis is the most predominant.
__Response: __We have complied with the reviewer suggestion. Figure 1G now shows staged seminiferous tubules, and we have replaced the wild type image for one where the staged tubules match the knockout image.
7) Figure S4B does not show an increase of cells at Pachytene stage but at Lepto/zygotene stage (as well as an increase of spermatogonia). Please comment this discrepancy with results shown in Fig2.
__Response: __Figures 2 and S4 show distribution of cells in different substages of spermatogenesis and prophase I measured with very different methods: a cytological approach using chromosome spreads cells vs a transcriptomic approach that involves clustering of cells. We attribute the differences in cell type distribution to differences in the sensitivity of the methods to identify each cell type and therefore identify differences between the number of cells for each group. Moreover, our scRNA-seq data groups the leptotene and zygotene stages together, while the cytological approach allows for separation of these two sub-stages. Importantly, both results show that Ago413 spermatocytes are progressing slower from pachynema into diplonema and/or are dying after pachynema, as stated in line 194 in our manuscript.
8) Fig5H and 5I are not mentioned in the result section. Also, it would be useful to label them with "all chromosomes" and "XY" to differentiate them easily
__Response: __We apologize for the omission and have now cited Figures 5H and 5I in the manuscript (line 453). We have added the suggested labels.
9) Line 530 "data provide further evidence for a functional association between AGO-dependent small RNAs and heterochromatin formation, maintenance and/or silencing." Please rephrase, the present article does not really show that AGO nuclear role depends on small RNAs.
__Response____: __We agree with the reviewer that these data do not directly show a dependence on small RNAs. As our identified localization of AGO proteins to the pericentric heterochromatin coincides with localization of DICER shown previously by Yadav and collaborators (2020, doi: 10.1093/nar/gkaa460), we do believe that our data further implicates small RNAs in the silencing of heterochromatin. Yadav et al shows that DICER localizes to pericentromeric heterochromatin and processes major satellite transcripts into small RNAs in mouse spermatocytes, and cKO germ cells have reduced localization of SUV39H2 and H3K9me3 to the pericentromeric heterochromatin. Given the colocalization of both small RNA producing machinery and AGOs at pericentromeric heterochromatin, the AGOs may bind these small RNAs, and the statement in line 530 refers to how our results provide evidence for the involvement of other RNAi machinery in the silencing of pericentromeric heterochromatin investigated by Yadav et al which likely includes small RNAs.
To clarify this point, we have modified the text accordingly.
10) Line 1256: replace "cite here " by appropriate reference
__Response: __The reference was added to line 1256.
11) Please use SMARCA4 instead of BRG1 name as it is its official name.
__Response: __We have replaced BRG1 with SMARCA4 in the text and figures.
Figures:
Figure 1: Are the pictures shown for Ago3-tagged and floxed from the same stages ? The leptotene stage in 1A looks like a zygotene, while some pachytene/diplotene stage pictures do not look alike.
__Response: __New representative images have been added to figure 1 to match the same substages across the figure.
Figure 1D, please label the Y scale properly (testis weight related to body weight)
__Response: __We have fixed this.
FigS1: Please comment the presence of non-specific bands in the figure legend
__Response: __We have added a sentence in Figure S1 Legend.
Fig 2E and F, please indicate on the figure (in addition to its legend), what are the X and Y axes respectively to facilitate its reading.
__Response: __X and Y axes are now labelled in Figure 2E and F.
2F: please use an easier abbreviation for Spermatocyte than Sp (which could spermatogonia, sperm etc..) such as Scyte I ? (same comment for Fig 3C)
Response: The abbreviation for spermatocyte was changed from Sp to Scyte I in Figures 2 and 3.
Overall, for all figures showing GSEA analyses, could the authors explain what a High positive NES and a High negative NES mean in the results section?
Response: Thank you for this suggestion. We have added this information where the GSEA score of the cell markers is initially introduced.
Significance
Ago proteins are known for their roles in post transcriptional gene regulation via small RNA mediated cleavage of mRNA, which takes places in the cytoplasm. Some Ago proteins have been shown to be also located in the nucleus suggesting other non-canonical roles. It is the case of Ago4 which has been shown to localize to the transcriptionally silenced sex chromosomes (called sex body) of the spermatocyte nucleus, where it contributes to regulate their silencing (Modzelewski et al 2012). Interestingly, Ago4 knockout leads to Ago3 upregulation, including on the sex body indicating that Ago3 and Ago4 are involved in the same nuclear process. In their manuscript, de las Mercedes Carro et al., investigate the consequences of loss of both Ago3 and Ago4 in the male germline by the production of a triple knockout of Ago1, 3 and 4 in the mouse. With this model, the authors describe the role of Ago3 and Ago4 during spermatogenesis and show that they are involved in sex chromosome gene repression in spermatocytes and in round spermatids, as well as in the control of autosomal meiotic gene expression. Triple KO males have impaired meiosis and spermiogenesis, with fewer and abnormal spermatozoa resulting in reduced fertility. Since Ago1 male germline expression is restricted to pre-meiotic germ cells, it is not expected to contribute to the meiotic and postmeiotic phenotypes observed in the triple KO. The strengths of the study are i) the thorough analyses of mRNA expression at the single cell level, and in purified spermatocytes and spermatids (bulk RNAseq), ii) the identification of novel nuclear partners of AGO3/4 relevant for their described nuclear role: ATF2, which they show to also co-localize with the sex body, and BRG1/SMARCA4, a SWI/SNF chromatin remodeler. The main limitation of the study is the lack of information in the method regarding the production of the triple KO, as well as some aspects of the transcriptome and motif analyses. It is also surprising to see that the triple KO does not recapitulate the miRNA deregulation observed in Ago4 KO. The characterization of a non-canonical role of AGO3/4 in male germ cells will certainly influence researchers of the field, and also interest a broader audience studying Argonaute proteins and gene regulation at transcriptional and posttranscriptional levels.
Reviewer #2
Evidence, reproducibility and clarity
In the manuscript titled "Argonaute proteins regulate the timing of the spermatogenic transcriptional program" by Carro et al., the authors present their findings on how Argonaute proteins regulate spermatogenic development. They utilize a mouse model featuring a deletion of the gene cluster on chromosome 4 that contains Ago1, Ago3, and Ago4 to investigate the cumulative roles of AGO3 and AGO4 in spermatogenic cells. The authors characterize the distribution of AGO proteins and their effects on key meiotic milestones such as synapsis, recombination, meiotic transcriptional regulation, and meiotic sex chromosome inactivation (MSCI). They analyze stage-specific transcriptomes in spermatogenic cells using single-cell and bulk RNA sequencing and determine the interactome of AGO3 and AGO4 through mass spectrometry to examine how AGO proteins may regulate gene expression in these cells during meiotic and post-meiotic development. The authors conclude that both AGO3 and AGO4 are essential for regulating the overall gene expression program in spermatogenic cells and specifically modulate MSCI to repress sex-linked genes in pachytene spermatocytes, which may be partially mediated by the proper distribution of DNA damage repair factors. Additionally, AGO3 is suggested to interact with the chromatin remodeler SWI/SNF factor BRG1, facilitating its removal from the sex-chromatin to enable the repression of sex-linked genes during MSCI.
Major Comments: 1. The study utilized a triple knockout mouse model to determine the effect of AGO3 on spermatogenesis, following up on their previous report about the role of AGO4 in spermatogenesis, which resulted from an upregulation of AGO3 in Ago4-/- spermatocytes. However, the results are more difficult to interpret and ascertain the role of AGO3 in these cells, given the absence of any observable phenotype from Ago3 interruption. AGO4 regulates sex body formation, meiotic sex chromosome inactivation (MSCI), and miRNA production in spermatocytes, all of which were noted in the absence of both AGO3 and AGO4, with only an increased incidence of cells containing abnormal RNAPII at the sex chromosomes. It will be necessary to characterize how AGO3 regulates spermatogenic development, including meiotic progression and the regulation of the meiotic transcriptome, and compare these findings with the current observations to determine if the proposed mechanism involving AGO3, BRG1, and possibly AP2 is relevant in this context.
__Response: __While we agree with Reviewer that a single Ago3 knockout will help understand distinct roles of AGO3 and AGO4 in spermatogenesis, the time and resources required to generate a new mouse model are substantial. The analysis included in this current manuscript has already taken over seven years, and with the lengthy production of a new single mutant mouse, validation of the new mouse, and then final analysis, we would be looking at another 3-5 years of analysis. In the current funding climate, and with strong concerns over ensuring reduction in utilization of laboratory mice, we consider this request to be far in excess of what is required to move this important story forward.
The Ago413-/- mouse model has allowed us to associate a nuclear role of Argonaute proteins with a strong reproductive phenotype in the mouse germline. Given the redundancy between Ago3 and Ago4, it is likely that a single Ago3 knockout would have a mild phenotype just like the Ago4 KO. All this said, we agree with the reviewer that analysis of an Ago3 knockout mouse is a valuable next step, just not within this chapter of the story.
- Does Ago413-/- mice recapitulate the early meiotic entry phenotype observed in Ago4-/- mice? If not, could it be possible that AGO3 promotes meiotic entry, given its strong mRNA expression in spermatogonia according to the scRNAseq data (Fig. 2B)
Response: Our scRNA-seq data shows strong expression of Ago3 in spermatogonia, as mentioned by the Reviewer. Analysis of cell cycle marker expression also shows that the transcriptomic profile of spermatogonia is altered, with higher levels of transcripts corresponding to the later G2/M stages (Figure 2D). Moreover, Ago413 knockouts present an increase in the number of spermatogonial stem cells (Supplementary Figure S4B). However, this cluster represents a pool of quiescent and mitotically active cells entering meiosis, therefore interpretation of these data might be challenging. While specific experiments could be conducted to answer this question, this is outside of the scope of our manuscript. The manuscript as it stands is already rather large, and a full analysis of meiotic entry dynamics would dilute the core message relating to chromatin regulation in the sex body.
- The authors suggested that the removal of BRG1 by AGO3 is necessary during sex body formation and the eventual establishment of MSCI. However, the BAF complex subunit ARID1A has been shown to facilitate MSCI by regulating promoter accessibility. It will be interesting to determine how BRG1 distribution changes across the genome in the absence of AGO proteins and how that correlates with alterations in sex-linked gene expression.
__Response: __We agree that changes in BRG1 distribution across the genome would be very interesting to identify. However, in this work we show that BRG1/SMARCA4 protein changes its localization in the sex body very rapidly between early to late pachynema. These two substages are only discernable by immunofluorescence using synaptonemal complex markers, as there are currently no available techniques to enrich for these subfractions. Therefore, study of genome occupancy of BRG1 in these specific substages by techniques such as CUT&Tag are not currently possible. However, we are currently working on new methods to distinguish these cell populations and hope eventually to use these purification strategies to perform the studies suggested by this reviewer. Alternatively, the hope is that single cell CUT&Tag methods will become more reliable, and will enable us to address these questions. Both of these options are not currently available to us. The studies by Menon et al (2024-doi:10.7554/eLife.88024.5) provide strong evidence to support that ARID1A is needed to reduce promoter accessibility of XY silenced genes in prophase I through modulation of H3.3 distribution. However, this mechanism and our identification of the removal of BRG1 between early and late pachytema are not inconsistent with one another, as either SMARCA4 or SMARCA2 can associate with ARID1A as part of the cBAF complex, and ARID1A is also not in all forms of the BAF complex which BRG1 are in. The difference between our results and those seen in Menon et al likely indicate that there are multiple forms of the BAF complex which are differentially regulated during MSCI and play different roles in silencing transcription. Further studies of specific BAF subunits are needed to elucidate how different flavors of the BAF complex act at specific genomic locations and meiotic time points.
- The observations presented in this manuscript (Fig. 1D, 2C, 3D, and 4) suggest a haploinsufficiency of the deleted locus in spermatogenic development. How does this compare with the ablation of either Ago3 or Ago4? Please explain.
Response: Our previous studies in single Ago4 knockouts did not present a heterozygous phenotype (Modzelewski et al 2012, doi: 10.1016/j.devcel.2012.07.003, data not shown). Triple Ago413 knockouts show a much stronger fertility phenotype than single Ago4 knockout. Testis weight of Ago413 homozygous null present a 30% reduction while heterozygous mice show a 15% reduction (Figure 1D), comparable to the 13% reduction previously observed in Ago4-/- males. Sperm counts of Ago413 null and heterozygous males are reduced by 60% and 39% compared to wild type (Figure 1E), respectively, whereas Ago4 null mice have a milder phenotype, with only a 22% reduction in sperm counts. At the MSCI level, both homozygous and heterozygous Ago413 mutant spermatocytes show a similar increase in pachytene spermatocytes with increased RNA pol II ingression into the sex body with respect to wild-type of 35% and 30%, respectively. Ago4 single knockouts show an almost 18% increase in Pol II ingression when compared to wild type. These comparisons are now included in our manuscript in lines 170, 172 and 288. A milder phenotype of the Ago4 knockout and haploinsufficiency in triple Ago413 knockouts but not in Ago4 single knockouts is likely a consequence of the overlapping functions of Ago3 and Ago4 in mammals (and/or overexpression of Ago3 in Ago4 knockouts). In the context of their role in RISC, Wang et al (doi: 10.1101/gad.182758.111) studied the effects of single and double conditional knockouts for Ago1 and Ago2 in miRNA-mediated silencing. They discovered that the interaction between miRNAs and AGOs is highly correlated with the abundance of each AGO protein, and only double knockouts presented an observable phenotype.
Minor Comments: Based on the interactome analysis, it was argued that AGO3 and AGO4 may function separately. Please discuss how AGO3 might compensate for AGO4 (Line 109).
Response: We hypothesize that the combined function of AGO3 and AGO4 is needed for proper sex chromosome inactivation during meiosis. We base this hypothesis on the facts that (i) both proteins localize to the sex body in pachytene spermatocytes, (ii) loss of Ago4 leads to upregulation of Ago3, and (iii) the MSCI phenotype of Ago413 knockout mice is much stronger than the single Ago4 knockout (see above). However, AGO3 and AGO4 might not induce silencing through the same mechanism or pathway. In this work, we observed that their temporal expression in prophase I is different; while AGO3 protein seems to disappear by the diplotene stage, AGO4 is present in the sex body of these cells. Moreover, the proteomic analysis revealed a very low number of common interactors, an observation which could support the idea of AGO3 and AGO4 acting by different (albeit perhaps related) mechanisms to achieve MSCI. It is also possible that common interactors were not identified in our proteomic analysis due to the low abundance of AGO3 and AGO4 in the germ cells, limiting the resolution of the proteomics analysis (note that in order to visualize AGO proteins in WB experiments, at least 60 μg of enriched germ cell lysate must be loaded per lane). Moreover, given the difficulty in obtaining enough isolated pachytene and diplotene spermatocytes to perform immunoprecipitation experiments, we performed IP experiments in whole germ cell lysates, which limits the interpretation of our analysis. If AGO3 and AGO4 protein interactors overlap, then AGO3 would directly substitute for AGO4 leading to silencing in single Ago4 knockouts. However, if AGO3 and AGO4 work together through different, complementary mechanisms, then Ago4 mutant mice likely compensates loss of Ago4 by upregulation of Ago3along with specific interactors of the given pathway. We have added a sentence addressing this matter in line 411 of the results section and lines 506 and 513 of the discussion in the revised manuscript.
In Line 221, it is unclear what is meant by 'cell cycle transcripts'. Does this refer to meiotic transcripts? It is also important to discuss the relevance of the G2/M cell cycle marker genes at later stages of meiotic prophase.
Response: Thank you for this suggestion. We have changed the relevant text to remove redundancies and include more information. We agree that considering the importance of these genes across meiotic prophase is needed, as cells which are in the dividing stage will already have produced the proteins necessary for division. These cells likely correspond to the diplotene/M cluster cells that have a lower G2/M score, potentially causing the bimodal distribution seen in Figure 2D. We have added a sentence addressing this to the manuscript.
While identified as a common interactor of both AGO3 and AGO4 in lines 440-445, HNRNPD is not listed among AGO4 interactors in Table S6. Please correct or explain this discrepancy.
Response: HNRPD was originally identified as an AGO4 interactor using a less strict criteria than the one used in our manuscript: we required consistent enrichment in at least two rounds of IP MS experiments. This reference to HNRNPD was a mistake, given that HNRPD was only enriched in one of our three replicates. Thus, we apologize and have removed the sentence in lines 440-445.
It is unclear whether wild-type cell lysate or lysate containing FLAG-tagged AGO3 was used for BRG1 immunoprecipitation, and which antibody was used to detect AGO3 in the BRG1 IP sample. A co-IP experiment demonstrating interaction between BRG1 and wild-type AGO3 would be ideal in this context. Furthermore, co-localization by IF would be beneficial to determine the subcellular localization and the cell stages the interaction may be occurring. Additionally, co-IP and Western blot methodologies should be included in the methods section.
__Response: __MYC-FLAG tagged AGO3 protein lysates were used for BRG1 Co-Immunoprecipitation, along with an anti MYC antibody to detect AGO3. This is now detailed in the Methods section of our revised manuscript (line 1133).
Regarding BRG1 and AGO3 colocalization by IF, we can confidently show that both AGO3 and BRG1 localize to the sex chromosomes in early pachynema by comparing BRG1/SYCP3 and FLAG-AGO3/SYCP3 stained spreads. We were not able to show colocalization simultaneously on the same cells, given the lack of appropriate antibodies. Our anti FLAG antibody is raised in mouse, while anti BRG1 is raised in rabbit, therefore a non-rabbit, non-mouse anti SYCP3 would be needed to identify prophase I substages, and our lab does not possess such a validated antibody. However, we now have access to a multiplexing kit that allows to use same-species antibodies for immunofluorescence and we can perform these experiments for a revised manuscript.
__Response: __The methods section now includes description of co-IP methodologies (line 1132). Western Blot methodologies are explained in lane 718, under the "Immunoblotting" title.
In line 599, it is unclear what is meant by 'persistence of sex chromosome de-repression'. Please correct or clarify this.
Response: This sentence has been changed and reads: "The persistence of sex chromosome gene expression".
If possible, please add an illustration to summarize the findings together.
Response: We thank the reviewer for this suggestion, and have now added this in Figure 6
Significance
Overall, this study enhances the understanding of gene expression regulation by AGO proteins during spermatogenesis. Several approaches, including functional, histological, and molecular characterization of the triple knockout phenotype, were instrumental in elucidating the role of AGO proteins in MSCI and meiotic as well as postmeiotic gene regulation. The main limitation of the study is that it is challenging to appreciate the role of AGO3 in addition to the previously published role of AGO4 without the inclusion of necessary control groups. Furthermore, the mechanism of action for AGO proteins in meiotic gene regulation was left relatively unexplored. This study presents new findings that will be significant for the research community interested in gene regulation, chromatin biology, and reproductive biology with the above suggestions considered.
__Reviewer #3 (Evidence, reproducibility and clarity (Required)): __
The authors characterize a CRISPR-Cas9 mouse mutant that targets 3 genes that encode AGO family proteins, 2 of which are expressed during spermatogenesis (AGO3 and AGO4) and one that is said is not expressed, AGO1. This mouse mutant showed that AGO3 and AGO4 both contribute to spermatogenesis success as the "Ago413" mutation gave rise to an additive reduction in testis weight, due to spermatocyte apoptosis, and reduction in sperm count. Furthermore, they use insertion mouse mutants for Ago3 and Ago2 that express tagged versions of their corresponding proteins, which they use in combination with pan-AGO antibodies and Ago mutants to show differential expression and localization properties of AGO2, AGO3, and AGO4 (and the absence of AGO1) during spermatogenesis with a particular focus on meiotic prophase. They perform single-cell RNAseq and intricate analyses to demonstrate a change in distribution of meiotic stages in Ago413 mutants, and the overall cell cycle in spermatogonia and spermatocytes is altered. This analysis shows that the mutation leads to an inability to downregulate prior spermatogonia/spermatocyte stage transcripts in a timely manner. On the other hand, later-stage spermatocytes are abnormally expressing spermiogenesis genes. Similar to the Ago4 mutant previously characterized MSCI is disrupted. The authors also show that AGO3 has different interaction partners compared to AGO4 and focus their final assessment on a novel interaction partner of AGO3, BRG1. They show that this factor, which is involved in chromatin remodeling, is aberrantly localized to the sex body during meiotic prophase and diplonema. As BRG1 is involved in open chromatin, it is proposed that AGO3 restricts BRG1 (and related proteins) from the XY chromosome to ensure MSCI. Overall, this paper is very well constructed with mechanistic insights that make this a very impactful contribution to the research community. Major Comments:
- The abstract contains "Ago413-/- mouse" without any explanation of what that is. The abstract needs to be a stand-alone document that does not require any referencing for context.
Response: We have included a sentence describing Ago413 in line 27
Figure 2C. - The significance bars are confusing as they appear to overlap strangely.
Response: We have modified this figure and now present the significance bars are on top of the data points.
On line 235, the authors state that "we first identified the top non-overlapping upregulated genes for Ago413+/+ germ cells in each cluster. Why did the authors not also select down-regulated genes in each cluster to perform a similar analysis?
__Response: __Thank you for this question. As our goal was to identify genes that are markers of the transcriptional program in each cell type, we used only uniquely upregulated genes for each cluster. Genes that are downregulated for a cluster may be indicative of the transcription in several other cell types, which is not easily interpretable. For a revised manuscript, we will perform this analysis to determine if there is any specific alterations in these downregulated genes.
Their Ago413 mutant characterization does a good job of assessing meiotic prophase and spermatozoa. However, their assessment of the stages in between these is lacking (meiotic divisions and spermiogenesis).
Response: We understand the reviewer's concern, however, it is not usual to study stages between the first meiotic division and spermiogenesis because meiosis II is so rapid and thus we lack tools to dissect it. In general, any defect that impacts meiosis I (and particularly prophase I) leads to cell death during prophase I or at metaphase I due to strictly adhered checkpoints that eradicate defective cells. Thus, the increased TUNEL staining in prophase I indicates to us that defective cells are cleared before exit from meiosis I, and those cells progressing to the spermatid stage are "normal" for meiosis II progression. For these cells that did complete meiosis I and progressed normally through meiosis II, we analyzed their spermiogenic outcome extensively (see section entitled "Post-meiotic spermatids from Ago413-/- males exhibit defective spermiogenesis and poor spermatozoa function"). This section included extensive sperm morphology, sperm motility and sperm fertility through in vitro fertilization assays. That said, we have added a sentence on line 268 to explain the transit through meiosis II.
The discovery of the interaction between BRG1 and AGO3 is exciting. They should assess BRG1 localization in later sub-stages, including late diplonema and diakinesis.
__Response: __BRG1(SMARCA4) was analyzed throughout prophase I, as shown in image 5G, including quantification of fluorescence intensity included the analysis of diplonema (5H-I). However, diakinesis was not included here since there was no observable signal of BRG1 in these cells. We have explained this in lines 459.
ATF2 should have been assessed in more detail, as was done for BRG1 in Figure 5.
__Response: __We agree with the Reviewer, however, staining of chromosome spreads with the anti ATF2 antibody was not possible in our hands after several attempts and changes in staining conditions. However, as staining of sections was successful, we showed localization of ATF2 on spermatocytes by co staining sections with SYCP3 and ATF2.
Reviewer #3 (Significance (Required)): Overall, this paper is very well constructed with mechanistic insights, as described in my reviewer comments, that make this a very impactful contribution to the research community.
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Author response:
The following is the authors’ response to the original reviews
Public Reviews:
Reviewer #1 (Public review):
Summary:
The authors have used full-length single-cell sequencing on a sorted population of human fetal retina to delineate expression patterns associated with the progression of progenitors to rod and cone photoreceptors. They find that rod and cone precursors contain a mix of rod/cone determinants, with a bias in both amounts and isoform balance likely deciding the ultimate cell fate. Markers of early rod/cone hybrids are clarified, and a gradient of lncRNAs is uncovered in maturing cones. Comparison of early rods and cones exposes an enriched MYCN regulon, as well as expression of SYK, which may contribute to tumor initiation in RB1 deficient cone precursors.
Strengths:
(1) The insight into how cone and rod transcripts are mixed together at first is important and clarifies a long-standing notion in the field.
(2) The discovery of distinct active vs inactive mRNA isoforms for rod and cone determinants is crucial to understanding how cells make the decision to form one or the other cell type. This is only really possible with full-length scRNAseq analysis.
(3) New markers of subpopulations are also uncovered, such as CHRNA1 in rod/cone hybrids that seem to give rise to either rods or cones.
(4) Regulon analyses provide insight into key transcription factor programs linked to rod or cone fates.
(5) The gradient of lncRNAs in maturing cones is novel, and while the functional significance is unclear, it opens up a new line of questioning around photoreceptor maturation.
(6) The finding that SYK mRNA is naturally expressed in cone precursors is novel, as previously it was assumed that SYK expression required epigenetic rewiring in tumors.
We thank the reviewer for describing the study’s strengths, reflecting the major conclusions of the initially submitted manuscript. However, based on new analyses – including the requested analyses of other scRNA-seq datasets, our revision clarifies that:
- related to point (1), cone and rod transcripts do not appear to be mixed together at first (i.e., in immediately post-mitotic immature cone and rod precursors) but appear to be coexpressed in subsequent cone and rod precursor stages; and
- related to point (3), CHRNA1 appears to mark immature cone precursors that are distinct from the maturing cone and rod precursors that co-express cone- and rod-related RNAs (despite the similar UMAP positions of the two populations in our dataset).
Weaknesses:
(1) The writing is very difficult to follow. The nomenclature is confusing and there are contradictory statements that need to be clarified.
(2) The drug data is not enough to conclude that SYK inhibition is sufficient to prevent the division of RB1 null cone precursors. Drugs are never completely specific so validation is critical to make the conclusion drawn in the paper.
We thank the reviewer for noting these important issues. Accordingly, in the revised manuscript:
(1) We improve the writing and clarify the nomenclature and contradictory statements, particularly those noted in the Reviewer’s Recommendations for Authors.
(2) We scale back claims related to the role of SYK in the cone precursor response to RB1 loss, with wording changes in the Abstract, Results, and Discussion, which now recognize that the inhibitor studies only support the possibility that cone-intrinsic SYK expression contributes to retinoblastoma initiation, as detailed in our responses to Reviewer’s Recommendations for Authors. We agree and now mention that genetic perturbation of SYK is required to prove its role.
Reviewer #2 (Public review):
Summary:
The authors used deep full-length single-cell sequencing to study human photoreceptor development, with a particular emphasis on the characteristics of photoreceptors that may contribute to retinoblastoma.
Strengths:
This single-cell study captures gene regulation in photoreceptors across different developmental stages, defining post-mitotic cone and rod populations by highlighting their unique gene expression profiles through analyses such as RNA velocity and SCENIC. By leveraging fulllength sequencing data, the study identifies differentially expressed isoforms of NRL and THRB in L/M cone and rod precursors, illustrating the dynamic gene regulation involved in photoreceptor fate commitment. Additionally, the authors performed high-resolution clustering to explore markers defining developing photoreceptors across the fovea and peripheral retina, particularly characterizing SYK's role in the proliferative response of cones in the RB loss background. The study provides an in-depth analysis of developing human photoreceptors, with the authors conducting thorough analyses using full-length single-cell RNA sequencing. The strength of the study lies in its design, which integrates single-cell full-length RNA-seq, longread RNA-seq, and follow-up histological and functional experiments to provide compelling evidence supporting their conclusions. The model of cell type-dependent splicing for NRL and THRB is particularly intriguing. Moreover, the potential involvement of the SYK and MYC pathways with RB in cone progenitor cells aligns with previous literature, offering additional insights into RB development.
We thank the reviewer for summarizing the main findings and noting the compelling support for the conclusions, the intriguing cell type-dependent splicing of rod and cone lineage factors, and the insights into retinoblastoma development.
Weaknesses:
The manuscript feels somewhat unfocused, with a lack of a strong connection between the analysis of developing photoreceptors, which constitutes the bulk of the manuscript, and the discussion on retinoblastoma. Additionally, given the recent publication of several single-cell studies on the developing human retina, it is important for the authors to cross-validate their findings and adjust their statements where appropriate.
We agree that the manuscript covers a range of topics resulting from the full-length scRNAseq analyses and concur that some studies of developing photoreceptors were not well connected to retinoblastoma. However, we also note that the connection to retinoblastoma is emphasized in several places in the Introduction and throughout the manuscript and was a significant motivation for pursuing the analyses. We suggest that it was valuable to highlight how deep, fulllength scRNA-seq of developing retina provides insights into retinoblastoma, including i) the similar biased expression of NRL transcript isoforms in cone precursors and RB tumors, ii) the cone precursors’ co-expression of rod- and cone-related genes such as NR2E3 and GNAT2, which may explain similar co-expression in RB cells, and iii) the expression of SYK in early cones and RB cells. While the earlier version had mainly highlighted point (iii), the revised Discussion further refers to points (i) and (ii) as described further in the response to the Reviewer’s Recommendations for Authors.
We address the Reviewer’s request to cross-validate our findings with those of other single-cell studies of developing human retina by relating the different photoreceptor-related cell populations identified in our study to those characterized by Zuo et al (PMID 39117640), which was specifically highlighted by the reviewer and is especially useful for such cross-validation given the extraordinarily large ~ 220,000 cell dataset covering a wide range of retinal ages (pcw 8–23) and spatiotemporally stratified by macular or peripheral retina location. Relevant analyses of the Zuo et al dataset are shown in Supplementary Figures S3G-H, S10B, S11A-F, and S13A,B.
Reviewer #3 (Public review):
Summary:
The authors use high-depth, full-length scRNA-Seq analysis of fetal human retina to identify novel regulators of photoreceptor specification and retinoblastoma progression.
Strengths:
The use of high-depth, full-length scRNA-Seq to identify functionally important alternatively spliced variants of transcription factors controlling photoreceptor subtype specification, and identification of SYK as a potential mediator of RB1-dependent cell cycle reentry in immature cone photoreceptors.
Human developing fetal retinal tissue samples were collected between 13-19 gestational weeks and this provides a substantially higher depth of sequencing coverage, thereby identifying both rare transcripts and alternative splice forms, and thereby representing an important advance over previous droplet-based scRNA-Seq studies of human retinal development.
Weaknesses:
The weaknesses identified are relatively minor. This is a technically strong and thorough study, that is broadly useful to investigators studying retinal development and retinoblastoma.
We thank the reviewer for describing the strengths of the study. Our revision addresses the concerns raised separately in the Reviewer’s Recommendations for Authors, as detailed in the responses below.
Recommendations for the authors:
Reviewing Editor Comments:
The reviewers have completed their reviews. Generally, they note that your work is important and that the evidence is generally convincing. The reviewers are in general agreement that the paper adds to the field. The findings of rod/cone fate determination at a very early stage are intriguing. Generally, the paper would benefit from clarifications in the writing and figures. Experimentally, the paper would benefit from validation of the drug data, for example using RNAi or another assay. Alternatively, the authors could note the caveats of the drug experiments and describe how they could be improved. In terms of analysis, the paper would be improved by additional comparisons of the authors' data to previously published datasets.
We thank the reviewing editor for this summary. As described in the individual reviewer responses, we clarify the writing and figures and provide comparisons to previously published datasets (in particular, the large snRNA-seq dataset of Zuo et al., 2024 (PMID 39117640). With regard to the drug (i.e., SYK inhibitor) studies, we opted to provide caveats and describe the need for genetic approaches to validate the role of SYK, owing to the infeasibility of completing genetic perturbation experiments in the appropriate timeframe. We are grateful for the opportunity to present our findings with appropriate caveats.
Reviewer #1 (Recommendations for the authors):
Shayler cell sort human progenitor/rod/cone populations then full-length single cell RNAseq to expose features that distinguish paths towards rods or cones. They initially distinguish progenitors (RPCs), immature photoreceptor precursors (iPRPs), long/medium wavelength (LM) cones, late-LM cones, short wavelength (S) cones, early rods (ER) and late rods (LR), which exhibit distinct transcription factor regulons (Figures 1, 2). These data expose expected and novel enriched genes, and support the notion that S cones are a default state lacking expression of rod (NRL) or cone (THRB) determinants but retaining expression of generic photoreceptor drivers (CRX/OTX2/NEUROD1 regulons). They identify changes in regulon activity, such as increasing NRL activity from iPRP to ER to LR, but decreasing from iPRP to cones, or increasing RAX/ISL2/THRB regulon activity from iPRP to LM cones, but decreasing from iPRP to S cones or rods.
They report co-expression of rod/cone determinants in LM and ER clusters, and the ratios are in the expected directions (NRLTHRB or RXRG in ER). A novel insight from the FL seq is that there are differing variants generated in each cell population. Full-length NRL (FL-NRL) predominates in the rod path, whereas truncated NRL (Tr-NRL) does so in the cone path, then similar (but opposite) findings are presented for THRB (Fig 3, 4), whereas isoforms are not a feature of RXRG expression, just the higher expression in cones.
The authors then further subcluster and perform RNA velocity to uncover decision points in the tree (Figure 5). They identify two photoreceptor precursor streams, the Transitional Rods (TRs) that provide one source for rod maturation and (reusing the name from the initial clustering) iPRPs that form cones, but also provide a second route to rods. TR cells closest to RPCs (immediately post-mitotic) have higher levels of the rod determinant NR2E3 and NRL, whereas the higher resolution iPRPs near RPCs lack NR2E3 and have higher levels of ONECUT1, THRB, and GNAT2, a cone bias. These distinct rod-biased TR and cone-biased high-resolution iPRPs were not evident in published scRNAseq with 3′ end-counting (i.e. not FL seq). Regulon analysis confirmed higher NRL activity in TR cells, with higher THRB activity in highresolution iPRP cells.
Many of the more mature high-resolution iPRPs show combinations of rod (GNAT1, NR2E3) and cone (GNAT2, THRB) paths as well as both NRL and THRB regulons, but with a bias towards cone-ness (Figure 6). Combined FISH/immunofluorescence in fetal retina uncovers cone-biased RXRG-protein-high/NR2E3-protein-absent cone-fated cells that nevertheless expressed NR2E3 mRNA. Thus early cone-biased iPRP cells express rod gene mRNA, implying a rod-cone hybrid in early photoreceptor development. The authors refer to these as "bridge region iPRP cells".
In Figure 7, they identify CHRNA1 as the most specific marker of these bridge cells (overlapping with ATOH7 and DLL3, previously linked to cone-biased precursors), and FISH shows it is expressed in rod-biased NRL protein-positive and cone-biased RXRG proteinpositive cones at fetal week 12.
Figure 8 outlines the graded expression of various lncRNAs during cone maturation, a novel pattern.
Finally (Figure 9), the authors identify differential genes expressed in early rods (ER cluster from Figure 1) vs early cones (LM cluster, excluding the most mature opsin+ cells), revealing high levels of MYCN targets in cones. They also find SYK expression in cones. SYK was previously linked to retinoblastoma, so intrinsic expression may predispose cone precursors to transformation upon RB loss. They finish by showing that a SYK inhibitor blocks the proliferation of dividing RB1 knockdown cone precursors in the human fetal retina.
Overall, the authors have uncovered interesting patterns of biased expression in cone/rod developmental paths, especially relating to the isoform differences for NRL and THRB which add a new layer to our understanding of this fate choice. The analyses also imply that very soon after RPCs exit the cell cycle, they generate post-mitotic precursors biased towards a rod or cone fate, that carry varying proportions of mixed rod/cone determinants and other rod/cone marker genes. They also introduce new markers that may tag key populations of cells that precede the final rod/cone choice (e.g. CHRNA1), catalogue a new lncRNA gradient in cone maturation, and provide insight into potential genes that may contribute to retinoblastoma initiation, like SYK, due to intrinsic expression in cone precursors. However, as detailed below, the text needs to be improved considerably, and overinterpretations need to be moderated, removed, or tested more rigorously with extra data.
Major Comments
The manuscript is very difficult to follow. The nomenclature is at times torturous, and the description of hybrid rod/cone hybrid cells is confusing in many aspects.
(1) A single term, iPRP, is used to refer to an initial low-resolution cluster, and then to a subset of that cluster later in the paper.
We agree that using immature photoreceptor precursor (iPRP) for both high-resolution and lowresolution clusters was confusing. We kept this name for the low-resolution cluster (which includes both immature cone and immature rod precursors), renamed the high-resolution iPRP cluster immature cone precursors (iCPs). and renamed their transitional rod (TR) counterparts immature rod precursors (iRPs). These designations are based on
- the biased expression of THRB, ONECUT1, and the THRB regulon in iCPs (Fig. 5D,E);
- the biased expression of NRL, NR2E3, and NRL regulon iRPs (Fig. 5D,E);
- the partially distinct iCP and iRP UMAP positions (Figure 5C); and
- the evidence of similar immature cone versus rod precursor populations in the Zuo et al 3’ snRNA-seq dataset, as noted below and described in two new paragraphs starting at the bottom of p. 12.
(2) To complicate matters further, the reader needs to understand the subset within the iPRP referred to as bridge cells, and we are told at one point that the earliest iPRPs lack NR2E3, then that they later co-express NR2E3, and while the authors may be referring to protein and RNA, it serves to further confuse an already difficult to follow distinction. I had to read and re-read the iPRP data many times, but it never really became totally clear.
We agree that the description of the high-resolution iPRP (now “iCP”) subsets was unclear, although our further analyses of a large 3’ snRNA-seq dataset in Figure S11 support the impression given in the original manuscript that the earliest iCPs lack NR2E3 and then later coexpress NR2E3 while the earliest iRPs lack THRB and then later express THRB. As described in new text in the Two post-mitotic immature photoreceptor precursor populations section (starting on line 7 of p. 13):
When considering only the main cone and rod precursor UMAP regions, early (pcw 8 – 13) cone precursors expressed THRB and lacked NR2E3 (Figure S11D,E, blue arrows), while early (pcw 10 – 15) rod precursors expressed NR2E3 and lacked THRB (Figure S11D,E, red arrows), similar to RPC-localized iCPs and iRPs in our study (Figure 5D).
Next, as summarized in new text in the Early cone and rod precursors with rod- and conerelated RNA co-expression section (new paragraph at top of p. 16):
Thus, a 3’ snRNA-seq analysis confirmed the initial production of immature photoreceptor precursors with either L/M cone-precursor-specific THRB or rod-precursor-specific NR2E3 expression, followed by lower-level co-expression of their counterparts, NR2E3 in cone precursors and THRB in rod precursors. However, in the Zuo et al. analyses, the co-expression was first observed in well-separated UMAP regions, as opposed to a region that bridges the early cone and early rod populations in our UMAP plots. These findings are consistent with the notion that cone- and rod-related RNA co-expression begins in already fate-determined cone and rod precursors, and that such precursors aberrantly intermixed in our UMAP bridge region due to their insufficient representation in our dataset.
Importantly, and as noted in our ‘Public response’ to Reviewer 1, “CHRNA1 appears to mark immature cone precursors that are distinct from the maturing cone and rod precursors that coexpress cone- and rod-related RNAs (despite the similar UMAP positions of the two populations in our dataset).” In support of this notion, the immature cone precursors expressing CHRNA1 and other populations did not overlap in UMAP space in the Zuo et al dataset. We hope the new text cited above along with other changes will significantly clarify the observations.
(3) The term "cone/rod precursor" shows up late in the paper (page 12), but it was clear (was it not?) much earlier in this manuscript that cone and rod genes are co-expressed because of the coexpressed NRL and THRB isoforms in Figures 3/4.
We thank the reviewer for noting that the differential NRL and THRB isoform expression already implies that cone and rod genes are co-expressed. However, as we now state, the co-expression of RNAs encoding an additional cone marker (GNAT2) and rod markers (GNAT1, NR2E3) was
“suggestive of a proposed hybrid cone/rod precursor state more extensive than implied by the coexpression of different THRB and NRL isoforms” (first paragraph of “Early cone and rod …” section on p. 14; new text underlined).
(4) The (incorrect) impression given later in the manuscript is that the rod/cone transcript mixture applies to just a subset of the iPRP cells, or maybe just the bridge cells (writing is not clear), but actually, neither of those is correct as the more abundant and more mature LM and ER populations analyzed earlier coexpress NRL and THRB mRNAs (Figures 2, 3). Overall, the authors need to vastly improve the writing, simplify/clarify the nomenclature, and better label figures to match the text and help the reader follow more easily and clearly. As it stands, it is, at best, obtuse, and at worst, totally confusing.
We thank the reviewer for bringing the extent of the confusing terminology and wording to our attention. We revised the terminology (as in our response to point 1) and extensively revised the text. We also performed similar analyses of the Zuo et al. data (as described in more detail in our response to Reviewer 2), which clarifies the distinct status of cells with the “rod/cone transcript mixture” and cells co-expressing early cone and rod precursor markers.
To more clearly describe data related to cells with rod- and cone-related RNA co-expression, we divided the former Figure 6 into two figures, with Figure 6 now showing the cone- and rodrelated RNA co-expression inferred from scRNA-seq and Figure 7 showing GNAT2 and NR2E3 co-expression in FISH analyses of human retina plus a new schematic in the new panel 7E.
To separate the conceptually distinct analyses of cone and rod related RNA co-expression and the expression of early photoreceptor precursor markers (which were both found in the so-called bridge region – yet now recognized to be different subpopulations), we separated the analyses of the early photoreceptor precursor markers to form a new section, “Developmental expression of photoreceptor precursor markers and fate determinants,” starting on p. 16.
Additionally, we further review the findings and their implications in four revised Discussion paragraphs starting at the bottom of p. 23).
(5) The data showing that overexpressing Tr-NRL in murine NIH3T3 fibroblasts blocks FL-NRL function is presented at the end of page 7 and in Figure 3G. Subsequent analysis two paragraphs and two figures later (end page 8, Figure 5C + supp figs) reveal that Tr-NRL protein is not detectable in retinoblastoma cells which derive from cone precursors cells and express Tr-NRL mRNA, and the protein is also not detected upon lentiviral expression of Tr-NRL in human fetal retinal explants, suggesting it is unstable or not translated. It would be preferable to have the 3T3 data and retinoblastoma/explant data juxtaposed. E.g. they could present the latter, then show the 3T3 that even if it were expressed (e.g. briefly) it would interfere with FL-NRL. The current order and spacing are somewhat confusing.
We thank the reviewer for this suggestion and moved the description of the luciferase assays to follow the retinoblastoma and explant data and switched the order of Figure panels 3G and 3H.
(6) On page 15, regarding early rod vs early cone gene expression, the authors state: "although MYCN mRNA was not detected....", yet on the volcano plot in Figure S14A MYCN is one of the marked genes that is higher in cones than rods, meaning it was detected, and a couple of sentences later: "Concordantly, the LM cluster had increased MYCN RNA". The text is thus confusing.
With respect, we note that the original text read, “although MYC RNA was not detected,” which related to a statement in the previous sentence that the gene ontology analysis identified “MYC targets.” However, given that this distinction is subtle and may be difficult for readers to recognize, we revised the text (now on p. 19) to more clearly describe expression of MYCN (but not MYC) as follows:
“The upregulation of MYC target genes was of interest given that many MYC target genes are also targets of MYCN, that MYCN protein is highly expressed in maturing (ARR3+) cone precursors but not in NRL+ rods (Figure 10A), and that MYCN is critical to the cone precursor proliferative response to pRB loss8–10. Indeed, whereas MYC RNA was not detected, the LM cone cluster had increased MYCN RNA …”
(7) The authors state that the SYK drug is "highly specific". They provide no evidence, but no drug is 100% specific, and it is possible that off-target hits are important for the drug phenotype. This data should be removed or validated by co-targeting the SYK gene along with RB1.
We agree that our data only show the potential for SYK to contribute to the cone proliferative response; however, we believe the inhibitor study retains value in that a negative result (no effect of the SYK inhibitor) would disprove its potential involvement. To reflect this, we changed wording related to this experiment as follows:
In the Abstract, we changed:
(1) “SYK, which contributed to the early cone precursors’ proliferative response to RB1 loss” To: “SYK, which was implicated in the early cone precursors’ proliferative response to RB1 loss.”
(2) “These findings reveal … and a role for early cone-precursor-intrinsic SYK expression.” To: “These findings reveal … and suggest a role for early cone-precursor-intrinsic SYK expression.”
In the last paragraph of the Results, we changed:
(1) “To determine if SYK contributes…” To: “To determine if SYK might contribute…”
(2) “the highly specific SYK inhibitor” To: “the selective SYK inhibitor”
(3) “indicating that cone precursor intrinsic SYK activity is critical to the proliferative response” To: “consistent with the notion that cone precursor intrinsic SYK activity contributes to the proliferative response.”
In the Results, we added a final sentence:
“However, given potential SYK inhibitor off-target effects, validation of the role of SYK in retinoblastoma initiation will require genetic ablation studies.”
In the Discussion (2nd-to-last paragraph), we changed:
“SYK inhibition impaired pRB-depleted cone precursor cell cycle entry, implying that native SYK expression rather than de novo induction contributes to the cone precursors’ initial proliferation.” To: “…the pRB-depleted cone precursors’ sensitivity to a SYK inhibitor suggests that native SYK expression rather than de novo induction contributes to the cone precursors’ initial proliferation, although genetic ablation of SYK is needed to confirm this notion.” In the Discussion last sentence, we changed:
“enabled the identification of developmental stage-specific cone precursor features that underlie retinoblastoma predisposition.” To: “enabled the identification of developmental stage-specific cone precursor features that are associated with the cone precursors’ predisposition to form retinoblastoma tumors.”
Minor/Typos
Figure 7 legend, H should be D.
We corrected the figure legend (now related to Figure 8).
Reviewer #2 (Recommendations for the authors):
(1) The author should take advantage of recently published human fetal retina data, such as PMID:39117640, which includes a larger dataset of cells that could help validate the findings. Consequently, statements like "To our knowledge, this is the first indication of two immediately post-mitotic photoreceptor precursor populations with cone versus rod-biased gene expression" may need to be revised.
We thank the reviewer for noting the evidence of distinct immediately post-mitotic rod and cone populations published by others after we submitted our manuscript. In response, we omitted the sentence mentioned and extensively cross-checked our results including:
- comparison of our early versus late cone and rod maturation states to the cone and rod precursor versus cone and rod states identified by Zuo et al (new paragraph on the top half of p. 6 and new figure panels S3G,H);
- detection of distinct immediately post-mitotic versus later cone and rod precursor populations (two new paragraphs on pp. 12-13 and new Figures S10B and S11A-E);
- identification of cone and rod precursor populations that co-express cone and rod marker genes (two new paragraphs starting at the bottom of p. 15 and new Figures S11D-F);
- comparison of expression patterns of immature cone precursor (iCP) marker genes in our and the Zuo et al dataset (new paragraph on top half of p. 17 and new Figure S13).
We also compare the cell states discerned in our study and the Zuo et al. study in a new Discussion paragraph (bottom of p. 23) and new Figure S17.
(2) The data generated comes from dissociated cells, which inherently lack spatial context. Additionally, it is unclear whether the dataset represents a pool of retinas from multiple developmental stages, and if so, whether the developmental stage is known for each cell profiled. If this information is available, the authors should examine the distribution of developmental stages on the UMAP and trajectory analysis as part of the quality control process.
We thank the reviewer for highlighting the importance of spatial context and developmental stage.
Related to whether the dataset represents a pool of retinae from multiple developmental stages, the different cell numbers examined at each time point are indicated in Figure S1A. To draw the readers’ attention to this detail, Figure S1A is now cited in the first sentence of the Results.
Related to the age-related cell distributions in UMAP plots, the distribution of cells from each retina and age was (and is) shown in Fig. S1F. In addition, we now highlight the age distributions by segregating the FW13, FW15-17, and FW17-18-19 UMAP positions in the new Figure 1C. We describe the rod temporal changes in a new sentence at the top of p. 5:
“Few rods were detected at FW13, whereas both early and late rods were detected from FW15-19 (Figure 1C), corroborating prior reports [15,20].”
We describe the cone temporal changes and note the likely greater discrimination of cell state changes that would be afforded by separately analyzing macula versus peripheral retina at each age in a new sentence at the bottom of p. 5:
“L/M cone precursors from different age retinae occupied different UMAP regions, suggesting age-related differences in L/M cone precursor maturation (Figure 1C).”
Moreover, they should assess whether different developmental stages impact gene expression and isoform ratios. It is well established that cone and rod progenitors typically emerge at different developmental times and in distinct regions of the retina, with minimal physical overlap. Grouping progenitor cells based solely on their UMAP positioning may lead to an oversimplified interpretation of the data.
(2a) We agree that different developmental stages may impact gene expression and isoform ratios, and evaluated stages primarily based on established Louvain clustering rather than UMAP position. However, we also used UMAP position to segregate so-called RPC-localized and nonRPC-localized iCPs and iRPs, as well as to characterize the bridge region iCP sub-populations. In the revision, we examine whether cell groups defined by UMAP positions helped to identify transcriptomically distinct populations and further examine the spatiotemporal gene expression patterns of the same genes in the Zuo et al. 3’ snRNA-seq dataset.
(2b) Related to analyses of immediately post-mitotic iRPs and iCPs, the new Figure S10A expanded the violin plots first shown in Figure 5D to compare gene expression in RPC-localized versus non-RPC-localized iCPs and iRPs and subsequent cone and rod precursor clusters (also presented in response to Reviewer 3). The new Figure S10C, shows a similar analysis of UMAP region-specific regulon activities. These figures support the idea that there are only subtle UMAP region-related differences in the expression of the selected gene and regulons.
To further evaluate early cone and rod precursors, we compared expression patterns in our cluster- and UMAP-defined cell groups to those of the spatiotemporally defined cell groups in the Zuo et al. 3’ snRNA-seq study. The results revealed similar expression timing of the genes examined, although the cluster assignments of a subset of cells were brought into question, especially the assigned rod precursors at pcw 10 and 13, as shown in new Figures S10B (grey columns) and S11, and as described in two new paragraphs starting near the bottom of p.12.
(2c) Related to analyses of iCPs in the so-called bridge region, our analyses of the Zuo et al dataset helped distinguish early cone and rod precursor populations (expressing early markers such as ATOH7 and CHRNA1) from the later stages exhibiting rod- and cone-related gene coexpression, which had intermixed in the UMAP bridge region in our dataset. Further parsing of early cone precursor marker spatiotemporal expression revealed intriguing differences as now described in the second half of a new paragraph at the top of p. 17, as follows:
“Also, different iCP markers had different spatiotemporal expression: CHRNA1 and ATOH7 were most prominent in peripheral retina with ATOH7 strongest at pcw 10 and CHRNA1 strongest at pcw 13; CTC-378H22.2 was prominently expressed from pcw 10-13 in both the macula and the periphery; and DLL3 and ONECUT1 showed the earliest, strongest, and broadest expression (Figure S13B). The distinct patterns suggest spatiotemporally distinct roles for these factors in cone precursor differentiation.”
(3) I would commend the authors for performing a validation experiment via RNA in situ to validate some of the findings. However, drawing conclusions from analyzing a small number of cells can still be dangerous. Furthermore, it is not entirely clear how the subclustering is done. Some cells change cell type identities in the high-resolution plot. For example, some iPRP cells from the low-resolution plots in Figure 1 are assigned as TR in high-resolution plots in Figure 5.
The authors should provide justification on the identifies of RPC localized iPRP and TR.
Comparison of their data with other publicly available data should strengthen their annotation
We agree that drawing conclusions from scRNA-seq or in situ hybridization analysis of a small number of cells can be dangerous and have followed the reviewer’s suggestion to compare our data with other publicly available data, focusing on the 3’ snRNA-seq of Zuo et al. given its large size and extensive annotation. Our analysis of the Zuo et al. dataset helped clarify cell identities by segregating cone and rod precursors with similar gene expression properties in distinct UMAP regions. However, we noted that the clustering of early cone and rod precursors likely gave numerous mis-assigned cells (as noted in response 2b above and shown in the new Figure S11). It would appear that insights may be derived from the combination of relatively shallow sequencing of a high number of cells and deep sequencing of substantially fewer cells.
Related to how subclustering was done, the Methods state, “A nearest-neighbors graph was constructed from the PCA embedding and clusters were identified using a Louvain algorithm at low and high resolutions (0.4 and 1.6)[70],” citing the Blondel et al reference for the Louvain clustering algorithm used in the Seurat package. To clarify this, the results text was revised such that it now indicates the levels used to cluster at low resolution (0.4, p. 4, 2nd paragraph) and at high resolution (1.6, top of p. 11) .
Related to the assignment of some iPRP cells from the low-resolution plots in Figure 1 to the TR cluster (now called the ‘iRP’ ‘cluster) in the high-resolution plots in Figure 5, we suggest that this is consistent with Louvain clustering, which does not follow a single dendrogram hierarchy.
The justification for referring to these groups as RPC-localized iCPs and iRPs relates to their biased gene and regulon expression in Fig. 5D and 5E, as stated on p. 12:
“In the RPC-localized region, iCPs had higher ONECUT1, THRB, and GNAT2, whereas iRPs trended towards higher NRL and NR2E3 (p= 0.19, p=0.054, respectively).”
(4) Late-stage LM5 cluster Figure 9 is not defined anywhere in previous figures, in which LM clusters only range from 1 to 4. The inconsistency in cluster identification should be addressed.
We revised the text related to this as follows:
“Indeed, our scRNA-seq analyses revealed that SYK RNA expression increased from the iCP stage through cluster LM4, in contrast to its minimal expression in rods (Figure 10E). Moreover, SYK expression was abolished in the five-cell group with properties of late maturing cones (characterized in Figure 1E), here displayed separately from the other LM4 cells and designated LM5 (Figure 10E).” (p. 19-20)
(5) Syk inhibitor has been shown to be involved in RB cell survival in previous studies. The manuscript seems to abruptly make the connection between the single-cell data to RB in the last figure. The title and abstract should not distract from the bulk of the manuscript focusing on the rod and cone development, or the manuscript should make more connection to retinoblastoma.
We appreciate the reviewer’s concern that the title may seem to over-emphasize the connection to retinoblastoma based solely on the SYK inhibitor studies. However, we suggest the title also emphasizes the identification and characterization of early human photoreceptor states, per se, and that there are a number of important connections beyond the SYK studies that could warrant the mention of cell-state-specific retinoblastoma-related features in the title.
Most importantly, a prior concern with the cone cell-of-origin theory was that retinoblastoma cells express RNAs thought to mark retinal cell types other than cones, especially rods. The evidence presented here, that cone precursors also express the rod-related genes helps resolve this issue. The issue is noted numerous times in the manuscript, as follows:
In the Introduction, we write:
“However, retinoblastoma cells also express rod lineage factor NRL RNAs, which – along with other evidence – suggested a heretofore unexplained connection between rod gene expression and retinoblastoma development[12,13]. Improved discrimination of early photoreceptor states is needed to determine if co-expression of rod- and cone-related genes is adopted during tumorigenesis or reflects the co-expression of such genes in the retinoblastoma cell of origin.” (bottom, p. 2) And:
“In this study, we sought to further define the transcriptomic underpinnings of human photoreceptor development and their relationship to retinoblastoma tumorigenesis.” (last paragraph, p. 3)
The Discussion also alluded to this issue and in the revised Discussion, we aimed to make the connection clearer. We previously ended the 3rd-to-last paragraph with,
“iPRP [now iCP] and early LM cone precursors’ expression of NR2E3 and NRL RNAs suggest that their presence in retinoblastomas[12,13] reflects their normal expression in the L/M cone precursor cells of origin.”
We now separate and elaborate on this point in a new paragraph as follows:
“Our characterization of cone and rod-related RNA co-expression may help resolve questions about the retinoblastoma cell of origin. Past studies suggested that retinoblastoma cells co-express RNAs associated with rods, cones, or other retinal cells due to a loss of lineage fidelity[12]. However, the early L/M cone precursors’ expression of NR2E3 and NRL RNAs suggest that their presence in retinoblastomas[12,13] reflects their normal expression in the L/M cone precursor cells of origin. This idea is further supported by the retinoblastoma cells’ preferential expression of cone-enriched NRL transcript isoforms (Figure S5B).” (middle of p. 24) Based on the above, we elected to retain the title.
Minor comments:
(1) It is difficult to see the orange and magenta colors in the Fig 3E RNA-FISH image. The colors should be changed, or the contrast threshold needs to be adjusted to make the puncta stand out more.
We re-assigned colors, with red for FL-NRL puncta and green for Tr-NRL puncta.
(2) Figure 5C on page 8 should be corrected to Supplementary Figure 5C.
We thank the reviewer for noting this error and changed the figure citation.
Reviewer #3 (Recommendations for the authors):
(1) Minor concerns
a. Abbreviation of some words needs to be included, example: FW.
We now provide abbreviation definitions for FW and others throughout the manuscript.
b. Cat # does not matches with the 'key resource table' for many reagents/kits. Some examples are: CD133-PE mentioned on Page # 22 on # 71, SMART-Seq V4 Ultra Low Input RNA Kit and SMARTer Ultra Low RNA Kit for the Fluidigm C1 Sytem on Page # 22 on # 77, Nextera XT DNA Library preparation kit on Page # 23 on # 77.
We thank the reviewer for noting these discrepancies. We have now checked all catalog numbers and made corrections as needed.
c. Cat # and brand name of few reagents & kits is missing and not mentioned either in methods or in key resource table or both. Eg: FBS, Insulin, Glutamine, Penicillin, Streptomycin, HBSS, Quant-iT PicoGreen dsDNA assay, Nextera XT DNA LibraryPreparation Kit, 5' PCR Primer II A with CloneAmp HiFi PCR Premix.
Catalog numbers and brand names are now provided for the tissue culture and related reagents within the methods text and for kits in the Key Resources Table. Additional descriptions of the primers used for re-amplification and RACE were added to the Methods (p. 28-29).
d. Spell and grammar check is needed throughout the manuscript is needed. Example. In Page # 46 RXRγlo is misspelled as RXRlo.
Spelling and grammar checks were reviewed.
(2) Methods & Key Resource table.
a. In Page # 21, IRB# needs to be stated.
The IRB protocols have been added, now at top of p. 26.
b. In Page # 21, Did the authors dissociate retinae in ice-cold phosphate-buffered saline or papain?
The relevant sentence was corrected to “dissected while submerged in ice-cold phosphatebuffered saline (PBS) and dissociated as described10.” ( p. 26)
c. In Page # 21, How did the authors count or enumerate the cell count? Provide the details.
We now state, “… a 10 µl volume was combined with 10 µl trypan blue and counted using a hemocytometer” (top of p. 27)
d. Why did the authors choose to specifically use only 8 cells for cDNA preparation in Page # 22? State the reason and provide the details.
The reasons for using 8 cells (to prevent evaporation and to manually transfer one slide-worth of droplets to one strip of PCR tubes) and additional single cell collection details are now provided as follows (new text underlined):
“Single cells were sorted on a BD FACSAria I at 4°C using 100 µm nozzle in single-cell mode into each of eight 1.2 µl lysis buffer droplets on parafilm-covered glass slides, with droplets positioned over pre-defined marks … . Upon collection of eight cells per slide, droplets were transferred to individual low-retention PCR tubes (eight tubes per strip) (Bioplastics K69901, B57801) pre-cooled on ice to minimize evaporation. The process was repeated with a fresh piece of parafilm for up to 12 rounds to collect 96 cells). (p. 27, new text underlined)
e. Key resource table does not include several resources used in this study. Example - NR2E3 antibody.
We added the NR2E3 antibody and checked for other omissions.
(3) Results & Figures & Figure Legends
a. Regulon-defined RPC and photoreceptor precursor states
i. On page # 4, 1 paragraph - Clarify the sentence 'Exclusion of all cells with <100,000 cells read and 18 cells.........Emsembl transcripts inferred'. Did the authors use 18 cells or 18FW retinae?
The sentence was changed to:
“After sequencing, we excluded all cells with <100,000 read counts and 18 cells expressing one or more markers of retinal ganglion, amacrine, and/or horizontal cells (POU4F1, POU4F2, POU4F3, TFAP2A, TFAP2B, ISL1) and concurrently lacking photoreceptor lineage marker OTX2. This yielded 794 single cells with averages of 3,750,417 uniquely aligned reads, 8,278 genes detected, and 20,343 Ensembl transcripts inferred (Figure S1A-C).” (p. 4, new words underlined)
To clarify that 18 retinae were used, the first sentence of the Results was revised as follows:
“To interrogate transcriptomic changes during human photoreceptor development, dissociated RPCs and photoreceptor precursors were FACS-enriched from 18 retinae, ages FW13-19 …” (p. 4).
Why did the authors 'exclude cells lacking photoreceptor lineage marker OTX2' from analysis especially when the purpose here was to choose photoreceptor precursor states & further results in the next paragraph clearly state that 5 clusters were comprised of cells with OTX2 and CRX expression. This is confusing.
We apologize for the imprecise diction. We divided the evidently confusing sentence into two sentences to more clearly indicate that we removed cells that did not express OTX2, as in the first response to the previous question.
ii. In Page # 5, the authors reported the number of cell populations (363 large and 5 distal) identified in the THRB+ L/M-cone cluster. What were the # of cell populations identified in the remaining 5 clusters of the UMAP space?
We added the cell numbers in each group to Fig. 1B. We corrected the large LM group to 366 cells (p. 5) and note 371 LM cells , which includes the five distal cells, in Figure 1B.
b. Differential expression of NRL and THRB isoforms in rod and cone precursors
i. In Figure 3B, the authors compare and show the presence of 5 different NRL isoforms for all the 6 clusters that were defined in 3A. However, in the results, the ENST# of just 2 highly assigned transcript isoforms is given. What are the annotated names of the three other isoforms which are shown in 3B? Please explain in the Results.
As requested, we now annotate the remaining isoforms as encoding full-length or truncated NRL in Fig. 3B and show isoform structures in new Supplementary Figure S4B. We also refer to each transcript isoform in the Results (p. 7, last paragraph) and similarly evaluate all isoforms in RB31 cells (Fig. S5B).
ii. What does the Mean FPM in the y-axis of Fig 3C refer to?
Mean FPM represents mean read counts (fragments per million, FPM) for each position across Ensembl NRL exons for each cluster, as now stated in the 6th line of the Fig. 3 legend.
iii. A clear explanation of the results for Figures 3E-3F is missing.
We revised the text to more clearly describe the experiment as follows:
“The cone cells’ higher proportional expression of Tr-NRL first exon sequences was validated by RNA fluorescence in situ hybridization (FISH) of FW16 fetal retina in which NRL immunofluorescence was used to identify rod precursors, RXRg immunofluorescence was used to identify cone precursors, and FISH probes specific to truncated Tr-NRL exon 1T or FL-NRL exons 1 and 2 were used to assess Tr-NRL and FL-NRL expression (Figure 3E,F).” (p. 8, new text underlined).
c. Two post-mitotic photoreceptor precursor populations
i. Although deep-sequencing and SCENIC analysis clarified the identities of four RPC-localized clusters as MG, RPC, and iPRP indicative of cone-bias and TR indicative of rod-bias. It would be interesting to see the discriminating determinant between the TR and ER by SCENIC and deep-sequencing gene expression violin/box plots.
We agree it is of interest to see the discriminating determinant between the TR [now termed iRP] and ER clusters by SCENIC and deep-sequencing gene expression violin/box plots. We now provide this information for selected genes and regulons of interest in the new Supplementary Figures S10A and S10C, along with a similar comparison between the prior high-resolution iPRP (now termed iCP) cluster and the first high-resolution LM cluster, LM1, as described for gene expression on p. 12:
“Notably, THRB and GNAT2 expression did not significantly change while ONECUT1 declined in the subsequent non-RPC-localized iCP and LM1 stages, whereas NR2E3 and NRL dramatically increased on transitioning to the ER state (Figure S10A).”
And as described for regulon activities on pp. 13-14:
“Finally, activities of the cone-specific THRB and ISL2 regulons, the rod-specific NRL regulon, and the pan-photoreceptor LHX3, OTX2, CRX, and NEUROD1 regulons increased to varying extents on transitioning from the immature iCP or iRP states to the early-maturing LM1 or ER states (Figure 10C).”
We also show expression of the same genes for spatiotemporally grouped cells from the Zuo et al. dataset in the new Figure S10B, which displays a similar pattern (apart from the possibly mixed pcw 10 and pcw13 designated rod precursors).
d. Early cone precursors with cone- and rod-related RNA expression
i. On page #12, the last paragraph where the authors explain the multiplex RNA FISH results of RXRγ and NR2E3 by citing Figure S8E. However, in Fig S8E, the authors used NRL to identify the rods. Please clarify which one of the rod markers was used to perform RNA FISH?
Figure S8E (where NRL was used as a rod marker) was cited to remind readers that RXRg has low expression in rods and high expression in cones, rather than to describe the results of this multiplex FISH section. To avoid confusion on this point, Figure S8E is now cited using “(as earlier shown in Figure S8E).” With this issue clarified, we expect the markers used in the FISH + IF analysis will be clear from the revised explanation,
“… we examined GNAT2 and NR2E3 RNA co-expression in RXRg+ cone precursors in the outermost NBL and in RXRg+ rod precursors in the middle NBL … .” (p. 14-15).
To provide further clarity, we provide a diagram of the FISH probes, protein markers, and expression patterns in the new Figure 7E.
ii. The Y-axis of Fig 6G-6H needs to be labelled.
The axes have been re-labeled from “Nb of cells” to “Number of RXRg+ outermost NBL cells in each region” (original Fig. 6G, now Fig. 7C) and “Number of RXRg+ middle NBL cells in each region” (original Fig. 6H, now Fig. 7D).
iii. The legends of Figures 6G and 6H are unclear. In the Figure 6G legend, the authors indicate 'all cells are NR2E3 protein-'. Does that imply the yellow and green bars alone? Similarly, clarify the Figure 6H legend, what does the dark and light magenta refer to? What does the light magenta color referring to NR2E3+/ NR2E3- and the dark magenta color referring to NR2E3+/ NR2E3+ indicate?
We regret the insufficient clarity. We revised the Fig. 6G (now Fig. 7C) key, which now reads
“All outermost NBL cells are NR2E3 protein-negative.” We added to the figure legend for panel 7C,D “(n.b., italics are used for RNAs, non-italics for proteins).” The new scheme in Figure 7E shows the RNAs in italics proteins in non-italics. We hope these changes will clarify when RNA or protein are represented in each histogram category.
Overall, the results (on page # 13) reflecting Figures 6E-6H & Figure S11 are confusing and difficult to understand. Clear descriptions and explanations are needed.
We revised this results section described in the paragraph now spanning p. 14:
- We now refer to the bar colors in Figures 7C and 7D that support each statement.
- We provide an illustration of the findings in Figure 7E.
iv. Previously published literature has shown that cells of the inner NBL are RXRγ+ ganglion cells. So, how were these RXRγ+ ganglion cells in the inner NBL discriminated during multiplex RNA FISH (in Fig 6E-6H and in Fig S11)?
We thank the reviewer for requesting this clarification. We agree that “inner NBL” is the incorrect term for the region in which we examined RXRg+ photoreceptor precursors, as this could include RXRγ+ nascent RGCs. We now clarify that
“we examined GNAT2 and NR2E3 RNA co-expression in RXRg+ cone precursors in the outermost NBL and in RXRg+ rod precursors in the middle NBL … .” (p. 14-15) We further state,
“Limiting our analysis to the outer and middle NBL allowed us to disregard RXRγ+ retinal ganglion cells in the retinal ganglion cell layer or inner NBL (top of p. 15)”
Figure 7E is provided to further aid the reader in understanding the positions examined, and the legend states “RXRg+ retinal ganglion cells in the inner NBL and ganglion cell layer not shown.
v. In Figure 6E, what marker does each color cell correspond to?
In this figure (now panel 7A), we declined to provide the color key since the image is not sufficiently enlarged to visualize the IF and FISH signals. The figure is provided solely to document the regions analyzed and readers are now referred to “see Figure S12 for IF + FISH images” (2nd line, p. 15), where the marker colors are indicated.
vi. In Figure S11 & 6E, Protein and RNA transcript color of NR2E3, GNAT2 are hard to distinguish. Usage of other colors is recommended.
We appreciate the reviewer’s concern related to the colors (in the now redesignated Figure S12 and 7A); however, we feel this issue is largely mitigated by our use of arrows to point to the cells needed to illustrate the proposed concepts in Figure S12B. All quantitation was performed by examining each color channel separately to ensure correct attribution, which is now mentioned in the Methods (2nd-to-last line of Quantitation of FISH section, p. 35).
vii.
With due respect, we suggest that labeling each box (now in Figure 8B) makes the figure rather busy and difficult to infer the main point, which is that boxed regions were examined at various distanced from the center (denoted by the “C” and “0 mm”) with distances periodically indicated. We suggest the addition of such markers would not improve and might worsen the figure for most readers.
e. An early L/M cone trajectory marked by successive lncRNA expression
i. In Figure 8C - color-coded labelling of LM1-4 clusters is recommended.
We note Fig. 8C (now 9C) is intended to use color to display the pseudotemporal positions of each cell. We recognize that an additional plot with the pseudotime line imposed on LM subcluster colors could provide some insights, yet we are unaware of available software for this and are unable to develop such software at present. To enable readers to obtain a visual impression of the pseudotime vs subcluster positions, we now refer the reader to Figure 5A in the revised figure legend, as follows: (“The pseudotime trajectory may be related to LM1-LM4 subcluster distributions in Figure 5A.”).
ii. In Figure 8G - what does the horizontal color-coded bar below the lncRNAs name refer to? These bars are similar in all four graphs of the 8G figure.
As stated in the Fig. 8G (now 9G) legend, “Colored bars mark lncRNA expression regions as described in the text.” We revised the text to more clearly identify the color code. (p. 18-19)
f. Cone intrinsic SYK contributions to the proliferative response to pRB loss
i. In Fig 9F - The expression of ARR3+ cells (indicated by the green arrow in FW18) is poorly or rarely seen in the peripheral retina.
We thank the reviewer for finding this oversight. In panel 9F (now 10F), we removed the green arrows from the cells in the periphery, which are ARR3- due to the immaturity of cones in this region.
ii. In Figure 9F - Did the authors stain the FW16 retina with ARR3?
Unfortunately, we did not stain the FW16 retina for ARR3 in this instance.
iii. Inclusion of DAPI staining for Fig 9F is recommended to justify the ONL & INL in the images.
We regret that we are unable to merge the DAPI in this instance due to the way in which the original staining was imaged. A more detailed analysis corroborating and extending the current results is in progress.
iv. Immunostaining images for Figure 9G are missing & are required to be included. What does shSCR in Fig 9G refer to?
We now provide representative immunostaining images below the panel (now 10G). The legend was updated: “Bottom: Example of Ki67, YFP, and RXRg co-immunostaining with DAPI+ nuclei (yellow outlines). Arrows: Ki67+, YFP+, RXRg+ nuclei.” The revised legend now notes that shSCR refers to the scrambled control shRNA.
v. For Figure 9H - Is the presence and loss of SYK activity consistent with all the subpopulations (S & LM) of early maturing and matured cones?
We appreciate the reviewer’s question and interest (relating to the redesignated Figure 10H); however, we have not yet completed a comprehensive evaluation of SYK expression in all the subpopulations (S & LM) of early maturing and matured cones and will reserve such data for a subsequent study. We suggest that this information is not critical to the study’s major conclusions.
vi. Figure 9A is not explained in the results. Why were MYCN proteins assessed along with ARR3 and NRL? What does this imply?
We thank the reviewer for noting that this figure (now Figure 10A) was not clearly described.
As per the response to Reviewer 1, point 6 , the text now states,
“The upregulation of MYC target genes was of interest given that many MYC target genes are also MYCN targets, that MYCN protein is highly expressed in maturing (ARR3+) cone precursors but not in NRL+ rods (Figure 10A), and that MYCN is critical to the cone precursor proliferative response to pRB loss [8–10].” (middle, p. 19, new text underlined).
Hence, the figure demonstrates the cone cell specificity of high MYCN protein. This is further noted in the Fig. 10a legend: “A. Immunofluorescent staining shows high MYCN in ARR3+ cones but not in NRL+ rods in FW18 retina.”
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Author Response
The following is the authors’ response to the original reviews.
First, the authors would like to thank the reviewers and editors for their thoughtful comments. The comments were used to guide our revision, which is substantially improved over our initial submission. We have addressed all comments in our responses below, through a combination of clarification, new analyses and new experimental data.
Reviewer #1 (Public Review):
In this manuscript, the authors identified and characterized the five C-terminus repeats and a 14aa acidic tail of the mouse Dux protein. They found that repeat 3&5, but not other repeats, contribute to transcriptional activation when combined with the 14aa tail. Importantly, they were able to narrow done to a 6 aa region that can distinguish "active" repeats from "inactive" repeats. Using proximal labeling proteomics, the authors identified candidate proteins that are implicated in Dux-mediated gene activation. They were able to showcase that the C-terminal repeat 3 binds to some proteins, including Smarcc1, a component of SWI/SNF (BAF) complex. In addition, by overexpressing different Dux variants, the authors characterized how repeats in different combinations, with or without the 14aa tail, contribute to Dux binding, H3K9ac, chromatin accessibility, and transcription. In general, the data is of high quality and convincing. The identification of the functionally important two C-terminal repeats and the 6 aa tail is enlightening. The work shined light on the mechanism of DUX function.
A few major comments that the authors may want to address to further improve the work:
We thank the reviewer for their efforts and constructive comments, which have guided our revisions.
1) The summary table for the Dux domain construct characteristics in Fig. 6a could be more accurate. For example, C3+14 clearly showed moderate weaker Dux binding and H3K9ac enrichment in Fig 3c and 3e. However, this is not illustrated in Fig. 6a. The authors may consider applying statistical tests to more precisely determine how the different Dux constructs contribute to DNA binding (Fig. 3c), H3K9ac enrichment (Fig. 3e), Smarcc1 binding (Fig. 5e), and ATAC-seq signal (Fig. 5f).
We thank the reviewer for this comment, and agree that there were some modest differences in construct characteristics that were not captured in the Summary Table (6a). To better reflect the differences between constructs, we added additional dynamic range to our depiction/scoring, and believe that the new scoring system provides sufficient qualitative range to capture the difference without imposing a statistical approach.
2) Another concern is that exogenous overexpressed Dux was used throughout the experiments. The authors may consider validating some of the protein-protein interactions using spontaneous or induced 2CLCs (where Dux is expressed).
We agree that it would be helpful to determine endogenous DUX interaction with our BioID candidates. Here, we attempted co-IPs for endogenous DUX protein with the DUX antibody and were unsuccessful, which indicated that the DUX antibody is useful for detection but not efficient in the primary IP. This is why we utilized the mCherry tag for DUX IP experiments, which worked exceptionally well.
3) It could be technically challenging, but the authors may consider to validate Dux and Smarcc1 interaction in a biologically more relevant context such as mouse 2-cell embryos where both proteins are expressed. Whether Smarcc1 binding will be dramatically reduced at 4-cell embryos due to loss of Dux expression?
While we agree that it would be interesting to validate the in vivo interaction of DUX and SMARCC1 in the early embryo, it is not technically feasible for us to conduct the experiment, as the IP would require thousands of two-cell embryos, and we have the issue of poor co-IP quality with the DUX antibody.
Reviewer #2 (Public Review):
In this manuscript, Smith et al. delineated novel mechanistic insights into the structure-function relationships of the C-terminal repeat domains within the mouse DUX protein. Specifically, they identified and characterised the transcriptionally active repeat domains, and narrowed down to a critical 6aa region that is required for interacting with key transcription and chromatin regulators. The authors further showed how the DUX active repeats collaborate with the C-terminal acidic tail to facilitate chromatin opening and transcriptional activation at DUX genomic targets.
Although this study attempts to provide mechanistic insights into how DUX4 works, the authors will need to perform a number of additional experiments and controls to bolster their claims, as well as provide detailed analyses and clarifications.
We thank this reviewer for their constructive comments, and have conducted several new analyses, additional experiments and clarifications – which have strengthened the manuscript in several locations. Highlights include a statistical approach to the similarity of mouse repeats to themselves and to orthologs (Figure S1d) and clarified interpretations, a wider dynamic range to better reflect changes in DUX construct behaviors (Figure 6a), and additional data on construct behavior, including ‘inactive’ constructs (e.g C1+14aa in Figure 1a,d, new ATAC-seq in Figure S1g), and active constructs such as C3+C5+14aa and C3+C514aa (in Figure S1b).
Reviewer #3 (Public Review):
Dux (or DUX4 in human) is a master transcription factor regulating early embryonic gene activation and has garnered much attention also for its involvement in reprogramming pluripotent embryonic stem cells to totipotent "2C-like" cells. The presented work starts with the recognition that DUX contains five conserved c. 100-amino acid carboxy-terminal repeats (called C1-C5) in the murine protein but not in that of other mammals (e.g. human DUX4). Using state-of-the-art techniques and cell models (BioID, Cut&Tag; rescue experiments and functional reporter assays in ESCs), the authors dissect the activity of each repeat, concluding that repeats C3 and C5 possess the strongest transactivation potential in synergy with a short C-terminal 14 AA acidic motif. In agreement with these findings, the authors find that full-length and active (C3) repeat containing Dux leads to increased chromatin accessibility and active histone mark (H3K9Ac) signals at genomic Dux binding sites. A further significant conclusion of this mutational analysis is the proposal that the weakly activating repeats C2 and C4 may function as attenuators of C3+C5-driven activity.
By next pulling down and identifying proteins bound to Dux (or its repeat-deleted derivatives) using BioID-LC/MS/MS, the authors find a significant number of interactors, notably chromatin remodellers (SMARCC1), a histone chaperone (CHAF1A/p150) and transcription factors previously (ZSCAN4D) implicated in embryonic gene activation.
The experiments are of high quality, with appropriate controls, thus providing a rich compendium of Dux interactors for future study. Indeed, a number of these (SMARCC1, SMCHD1, ZSCAN4) make biological sense, both for embryonic genome activation and for FSHD (SMCHD1).
A critical question raised by this study, however, concerns the function of the Dux repeats, apparently unique to mice. While it is possible, as the authors propose, that the weak activating C1, C2 C4 repeats may exert an attenuating function on activation (and thus may have been selected for under an "adaptationist" paradigm), it is also possible that they are simply the result of Jacobian evolutionary bricolage (tinkering) that happens to work in mice. The finding that Dux itself is not essential, in fact appears to be redundant (or cooperates with) the OBOX4 factor, in addition to the absence of these repeats in the DUX protein of all other mammals (as pointed out by the authors), might indeed argue for the second, perhaps less attractive possibility.
In summary, while the present work provides a valuable resource for future study of Dux and its interactors, it fails, however, to tell a compelling story that could link the obtained data together.
We appreciated the reviewer’s views regarding the high quality of the work and our generation of an important dataset of DUX interactors. We also appreciate the comments provided to improve the work, and have performed and included in the revised version a set of clarifications, additional analyses and additional experiments that have served to reinforce our main points and provide additional mechanistic links. We also agree that more remains to be done to understand the function and evolution of repeats C1, C2 and C4.
Reviewer #1 (Recommendations For The Authors):
1) For immuno-blots, authors may indicate the expected bands to help readers better understand the results.
Agreed, and we have included the predicted molecular weight of proteins in the Figure Legends. We note that our work shows that the C-terminal domains confer anomalous migration in SDS-PAGE.
2) Fig. 5b, a blot missing for the mCherry group?
Figure 5b is a volcano blot, so we believe the reviewer is referring to Figure 5d, which is a coimmunoprecipitation experiment between SMARCC1 and mCherry-tagged DUX constructs. However, we are unsure of the comment as an anti mCherry sample is present in that panel.
3) Line 99-100, Fig. S1d, it seems that repeat2, but not repeat3, is more similar to human DUX4 C-terminal region.
This comment and one by another reviewer have prompted us to re-examine the similarities of the DUX repeats, and we have new analyses (Figure S1d) and an alternative framing in the manuscript as a result. We have expanded on this in our response to Reviewer #2, point #1 – and direct the reviewer there for our expanded treatment.
4) There are a few references are misplaced. For example, line 48, the studies that reported the role of Dux in inducing 2CLCs should be from Hendrickson et al., 2017, De Iaco et al., 2017, and Whiddon et al., 2017. The authors may want to double check all references.
Thanks for pointing these out. These issues have been corrected in the manuscript.
5) In the materials & methods section, a few potential errors are noticed. For example, concentrations of PD0325901 and CHIR99021 in mESC medium appear ~1000-fold higher than standards.
Thanks – corrected.
Reviewer #2 (Recommendations For The Authors):
Major Points
1) Line 99 - The authors claimed that the "human DUX4 C-terminal region is most similar to the 3rd repeat of mouse DUX", but based on Supp. Fig. 1d, the human DUX4 C-term should be most similar to the 2nd repeat of mouse DUX. If this is indeed the case, it will undermine the rest of this study, since the authors claim that the 3rd repeat is transcriptionally active, whereas the 2nd repeat is transcriptionally inactive, and the bulk of this study largely focused on how the active repeats, not the inactive repeats, are critical in recruiting key transcriptional and chromatin regulators to induce the embryonic gene expression program.
We thank the reviewer for their comments here. Since submission,and as mentioned above for reviewer #1 we have revisited the issue of similarity of the DUX4 C-terminal region to the mouse C-terminal repeats, with a BLAST-based approach that is more rigorous and informed by statistics – which is in Author response table 1 and now in the manuscript as Figure S1d, and has affected our interpretation. Our prior work involved a simple % identity comparison table and we now appreciate that some of the similarity analyses did not meet statistical significance, and therefore we are unable to draw certain conclusions. We make the appropriate modifications in the text. For example, we no longer state that the DUX4 C-terminus appears to be most similar to mouse repeats 3 and 5. This does not affect the main conclusions of the paper regarding interactions of the C-terminus with chromatin-related proteins, only our speculation on which repeat might have represented the original single repeat in the mouse – an issue we think of some interest, but did not rise to the level of mentioning in the original or current abstract.
Author response table 1.
Parameters: PAM250 matrix. Gap costs of existence: 15 and extension: 3. Numbers represent e-value of each pairwise comparison
*No significant similarities found (>0.05).
2) In Supp Fig 1d, it seems that the rat DUX4 C-terminal region is most similar to the 4th repeat of mouse DUX, which according to the author is supposedly transcriptionally inactive. This weakens the authors justification that the 3rd or 5th repeat is likely the "parental repeat for the other four", and further echoes my concern in point 1 where the human DUX4 C-term is most similar to the 2nd (inactive) repeat of mouse DUX.
The reviewer’s point is well taken and is addressed in point #1 above.
3) In Fig. 1d, the authors showed that DUX4-containing C3 and C5, but lacking acidic tail, can promote MERVL::GFP expression, albeit to a slightly lower extent compared to FL. However, in Fig. 2b, C3 or C5 alone (lacking acidic tail) completely failed to promote MERVL::GFP expression. However, in the presence of the acidic tail, both versions were able to promote MERVL::GFP expression, similar to that of FL. The latter would suggest that it is the acidic tail that is crucial for MERVL::GFP expression, and this does not quite agree with Fig 1b, where C12345 (lacking acidic tail) was able to promote MERVL::GFP expression. Although C12345 did not activate MERVL to a similar level as FL, it is clearly proficient, compared to C3 or C5 alone (lacking acidic tail) where there is no increase in MERVL at all. Additional constructs will be helpful to clarify these points. For example, 'C3+C5 minus acidic tail' and 'HD1+HD2+acidic tail only' constructs.
We agree that constructs such as those mentioned would add to the work. First, we have done the additional construct HD1+HD2+14aa tail, which is presented as ΔC12345+14aa in Figure 2a and in S2a. Additionally, we performed experiments on the requested C3+C5+14aa and C3+C5Δ14aa (see samples 6 and 7 in Author response image 1, which are now included in Supplemental Figure 2b). The results reinforce our hypothesis of an additive effect toward DUX target gene activation by increasing C-terminal repeats and including the 14aa tail.
Author response image 1.
4) Related to the above, the flow cytometry data for the MERVL::GFP reporter as presented in Figures 1 and 2, as well as in Supp. Fig. 2, show a considerably large difference in the %GFP|mCherry for the FL construct, ranging from ~6-26%. This makes it difficult to convince the reader which of the different DUX domain constructs cannot or can partially induce GFP|mCherry signal when compared to FL, and hence it is tough to definitively ascertain the exact contribution of each of the 5 C-terminal repeats with high confidence, as it appears that there exists a significant amount of variability in this MERVL::GFP reporter system. The authors need to address this issue since this is their primary method to elucidate the transcriptional activity of each of the mouse DUX repeat domains.
We note that with the Dux-/- cell lines we used throughout the timeline of the study, the percent of %GFP|mCherry expression progressively and slowly decreased – possibly due to slow/modest epigenetic silencing of the reporter. However, we always used the full-length DUX construct to establish the dynamic range. We emphasize that the relative differences between constructs over multiple cell line replicates remained relatively consistent. However, we elected to show absolute values in each experiment, rather than simply normalizing the full-length to 100% and showing relative.
5) Lines 140-142 - The authors claimed that the functional difference between the transcriptionally active and inactive repeats could be narrowed down to a "6aa region which is conserved between repeats C3 and C5, but not conserved in C1, C2 and C4". Assuming the 6aa sequence is DPLELF, why does C1C3a elicit almost twice the intensity of GFP|mCherry signal compared to C3C1c, despite both constructs having the exact same 6aa sequence?
Indeed, C1C3a and C3C1c both containing the ‘active’ DPL sequence but having different relative levels of %GFP|mCherry. This is consistent with these sequences having a positive role in DUX target gene regulation – but likely in combination with other other regions which potentiate its affect, possibly through interacting proteins or post-translational modifications.
Why does DPLEPL (the intermediate C3C1b construct) induce a similar extent of GFP|mCherry signal as the FL construct, even though the former includes 3aa from a transcriptionally inactive repeat? In contrast, GSLELF (the other intermediate C1C3b construct) that also includes 3aa from a transcriptionally inactive repeat is almost completely deficient in inducing any GFP|mCherry signal. Why is that so? Is DPL the most crucial sequence? It will be important to mutate these 3 (or the above 6) residues on FL DUX4 to examine if its transcriptional activity is abolished.
These are interesting points. DPL does appear to be the most important region in the mouse DUX repeats. However, DPL is not shared in the C-terminus of human DUX4. Notably, the DUX4 C-terminus is sufficient to activate the mouse MERVL::GFP reporter when cloned to mouse homeodomains (see Author response image 2, second sample) and other DUX target genes (initially published in Whiddon et al. 2017). One clear possibility is that the DPL region is helping to coordinate the additive effects of multiple DUX repeats, which only exist in the mouse protein.
Author response image 2.
6) Line 154 - The intermediate DUX domain construct C1C3b occupied a different position on the PCA plot from the C1C3c construct that does not contain any of the critical 6aa sequence, as shown in Fig. 2e. However, both these constructs appear to be similarly deficient in inducing any GFP|mCherry signal, as seen in Fig. 2c. Why is that so?
The PCA plot assesses the impact on the whole transcriptome and not just the MERVL::GFP reporter, suggesting the 3aa region has transcriptional effects on the genome beyond what is detected in the MERVL::GFP reporter.
7) To strengthen the claim that "Chromatin alterations at DUX bindings sites require a transcriptionally active DUX repeat", the authors should also perform CUT&Tag for constructs containing transcriptionally inactive DUX repeats (e.g. C1+14aa), and show that such constructs fail to occupy DUX binding sites, as well as are deficient in H3K9ac accumulation.
This is a good comment. We elected to control this with constructs containing or lacking an active repeat. Although we have not pursued this by CUT&TAG, we have examined the impact of DUX constructs with inactive repeats (including the requested C1+14aa, new Figure S1g) by ATAC-seq (see #12, ATAC-seq section, below), and observe no chromatin opening, suggesting that the lack of transcriptional activity is rooted in the inability to open chromatin.
8) It would be good if the authors could also include CUT&Tag data for some of the C1C3 chimeric constructs that were used in Fig. 2, since the authors argued that the minimal 6aa region is sufficient to activate many of the DUX target genes. This would also strengthen the authors’ case that the transcriptionally active, not inactive, repeats are critical for binding at DUX binding sites and ensuring H3K9ac occupancy.
We agree that these would be helpful, and have examined the inactive repeats in transcription and ATAC-seq formats during revision (new data in Figures 1d and S1g), but not yet the CUT&TAG format.
9) Line 213 - "SMARCA4" should have been "SMARCA5"? Based on Fig. 4d, SMARCA5 is picked up in the BirA*-DUX interactome, not SMARCA4.
Thanks – corrected.
10) Lines 250-252 - The authors compared the active BirA-C3 against the inactive BirA-C1 to elucidate the interactome of the transcriptionally active C3 repeat, as illustrated in Fig. 5c. They found 12 proteins more enriched in C1 and 154 proteins in C3. This information should be presented clearly as a separate tab in Supp Table 2. What are the proteins common to both constructs, i.e. enriched to a similar extent? Do they include chromatin remodellers too? Although the authors sought to identify differential interactors between the 2 constructs, it is also meaningful to perform 2 separate comparisons - active BirA-C3 against BirA alone control, and inactive BirA-C1 against BirA alone control - like in Fig. 4d, so as to more accurately define whether the active C3 repeat, and not the inactive C1 repeat, interacts with proteins involved in chromatin remodeling.
We thank the reviewer for this comment, and we have modified the manuscript by adding a second sheet in Supplementary Table 2 including the results for enriched proteins in BirA-C1 vs. C3. Additionally, due to limitations of annotation between BirA alone and BirA*-C3 being sequenced in different mass spectrometry experiments, it is difficult to quantitatively compare the two datasets with pairwise comparisons.
11) Fig 5d: The authors mentioned in the legend that endogenous IP was performed for SMARCC1. However, in line 266, they stated Flag-tagged SMARCC1. Is SMARCC1 overexpressed? The reciprocal IP should also be presented. More importantly, C1 constructs (e.g. C1+14aa and C1Δ14aa) should also be included.
To clarify, Figure 4e used exogenously overexpressed FLAG-SMARCC1 in HEK-293T cells to confirm the results of the full-length DUX BioID experiment. Figure 5d was performed with overexpressed DUX construct, but involved endogenous SMARCC1 in mESCs. This has now been made clearer in the revised manuscript.
12) For both the SMARCC1 CUT&Tag and ATAC-seq experiments shown in Figures 5e and 5f respectively, the authors need to include DUX derivatives that contain transcriptionally inactive repeats with and without the 14aa acidic tail, i.e. C1+14aa and C1Δ14aa, and show that these constructs prevent the binding/recruitment of SMARCC1 to DUX genomic targets, and correspondingly display a decrease in chromatin accessibility. Only then can they assert the requirement of the transcriptionally active repeat domains for proper DUX protein interaction, occupancy and target activation.
We agree that examination of an inactive repeat in certain approaches would improve the manuscript. Importantly, we have now included C1+14 in our ATAC-seq experiments, and in Author response image 3 two individual replicates, which constitute a new Figure S1g. Compared to the transcriptionally active DUX constructs, which see opening at DUX binding sites, we do not see chromatin opening at DUX binding sites with transcriptionally inactive C1+14.
Author response image 3.
13) To prove that DUX-interactors are important for embryonic gene expression, it will be important to perform loss of function studies. For instance, will the knockdown/knockout of SMARCC1 in cells expressing the active DUX repeat(s) lead to a loss of DUX target gene occupancy and activation?
We agree that it would be interesting to better understand SMARCC1 cooperation with DUX function in the embryo, but we believe this is beyond the scope of this paper.
Minor Points
1) Lines 124-126 - What is the reason/rationale for why the authors used one linker (GGGGS2) for constructs with a single internal deletion, but 2 different linkers (GGGGS2 and GAGAS2) for constructs with 2 internal deletions?
With Gibson cloning, there are homology overhang arms for each PCR amplicon that are required to be specific for each overlap. Additionally, each PCR amplicon needs to be specific enough from one another so that all inserts (up to 5 in this manuscript) are included and oriented in the right order. The linker sequences were included in the homology arm overlaps, so the nucleotide sequences for each linker needed to be specific enough to include all inserts. This is a general rule to Gibson cloning. Additionally, both GGGGS2 and GAGAS2 are common linker sequences used in molecular biology and the amino acids structures are similar to one another, suggesting there is no functional difference between linkers.
2) Line 704 - 705: In the figure legend, the authors stated that 'Constructs with a single black line have the linker GGGGS2 and constructs with two black lines have linkers with GGGGS2 and GAGAS2, respectively.'. This was not obvious in the figures.
Constructs used for flow and genomics experiments that are depicted in Figure 2, Supplementary Figure 2, Figure 3, Figure 4, and Figure 5 have depicted black lines where deletions are present. Where these deletions are present, there are linkers in order to preserve spacing and mobility for the protein.
3) Line 160 - Clusters #1 and #2 are likely written in the wrong order. It should have been "activating the majority of DUX targets in cluster #2, not cluster #1" and "failed to activate those in cluster #1, not cluster #2", based on the RNA-seq heatmap in Fig. 2f.
We thank the reviewer for this comment, and the error has been corrected in the manuscript.
4) Line 188 - Delete the word "of" in the following sentence fragment: "DUX binding sites correlating with the of transcriptional".
Thanks – corrected.
5) Line 191 - Delete the word "aids" in the following sentence fragment: "important for conferring H3K9ac aids at bound".
Thanks – corrected.
6) Line 711 - "C1-C3 a,b,d" should be "C1-C3 a,b,c".
Thanks – corrected.
7) Lines 711-712 - The colors "pink to blue" and "blue to pink" are likely written in the wrong order. Based on Fig. 2c, the blue to pink bar graphs should represent C1-C3 a,b,c in that order, and likewise the pink to blue bar graphs should represent C3-C1 a,b,c in that order.
Thanks – corrected.
8) There is an overload of data presented in Fig. 2c, such that it is difficult to follow which part of the figure represents each data segment as written in the figure legend. It is recommended that the data presented here is split into 2 sub-figures.
Figure 2c has a supporting figure in Supplementary Figure 2b. While there is both a graphical depiction of the constructions and the data both in the main panel of Figure 2C, we have depicted it as so to be as clear as possible for the reader to interpret the complexity and presentence of amino acids in each of the constructs.
9) Line 717 - "following" is misspelt.
Thanks – corrected.
10) Lines 720-721 - "(Top)" and "(Bottom)" should be replaced with "(Left)" and "(Right)", as the 2 bar graphs presented in Fig. 2d are placed side by side to each other, not on the top and bottom.
Thanks – corrected.
11) Lines 725 and 839 - "Principle" is misspelt. It should be "Principal".
Thanks – corrected.
12) In Figures 3d and 3e, the sample labeled "C3+14_1" should be re-labeled to "C3+14", in accordance with the other sub-figures. Additionally, for the sake of consistency, "aa" should be appended to the relevant constructs, e.g. "C3+14aa" and "C3Δ14aa".
Thanks – corrected.
13) Line 773 - Were the DUX domain constructs over-expressed for 12hr (as written in the figure legend) or 18hr (as labeled in Fig. 5d)?
Thanks – corrected.
14) Related to minor point 19 above, is there a reason/rationale for why some of the experiments used 12hr over-expression of DUX domain constructs (e.g. for CUT&TAG in Fig. 3), whereas in other experiments 18hr over-expression was chosen instead (e.g. flow cytometry for MERVL::GFP reporter in Figures 1 and 2, and co-IP validations of BirA*-DUX interactions in Fig. 4)?
Thanks for the opportunity to explain. In this work, experiments that reported on proteins that are translated following DUX gene activation (e.g. MERVL:GFP via flow) were done at 18hr to allow for enough time for transcription and translation of GFP (or other DUX target genes). For experiments that report on the impact of DUX on chromatin and transcription, such as RNA-seq, CUT&Tag, and ATAC-seq, we induced DUX domain constructs for 12 hours.
15) Line 804 - "ΔHDs" is missing between "C2345+14aa" and "ΔHD1".
Thanks – corrected.
16) In Fig. 5c, "Chromatin remodelers" is misspelt.
Thanks – corrected.
17) There is no reference in the manuscript to the proposed model that is presented in Fig. 6b.
Thanks – corrected.
Reviewer #3 (Recommendations For The Authors):
Given the uncertainty of the function of the Dux peptide repeats in mice, could it not also be possible that the underlying repeated nature of the (coding) DNA? That is, could these DNA repeats exert a regulatory function on Dux transcription itself (also given the dire consequences of misregulated DUX4 expression as seen in FSHD, for example).
Yes, it remains possible that the internal coding repeats within Dux are playing a role in locus regulation, and might be interesting to examine. However, we consider this question as being outside the scope of the current paper.
Finally, it would be interesting to know whether these repeats are, in fact, present in all mouse species. Already no longer present in rat, do they exist, or not, in more "distant" mice, e.g. M. caroli?
Determining whether all mouse strains contain C-terminal repeats in DUX is a question we also considered. However, Dux and its orthologs are present in long and very complex repeat arrays that are not present in the sequencing data or annotation in other mouse strains. Therefore, we are not unable to answer this question from existing sequencing data. Answering would require a considerable genome sequencing and bioinformatics effort, or alternatively a considerable effort aimed at cloning ortholog cDNAs from 2-cell embryos.
Minor points:
line 169: here it seems, in fact, that the 'inactive' C2, C4 repeats are more similar to each other (my calculation: 91 and 96% identity at the protein and DNA level, respectively) than the active C3 and C5 repeats (82 and 89% identity, resp.), the outlier being C1.
Thanks for this comment, which was mentioned by other reviewers as well and has been addressed through new statistical analyses and interpretation (see new Figure S1d).
line 191: I'm not sure this sentence parses correctly ("...14AA tail is important for conferring H3K9Ac aids at bound sites...")
We thank the reviewer for this comment, and we have corrected the sentence in the manuscript.
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For this, N-terminal GST-tag or C-terminal GFP-tag TRPV1 was transiently transfected into human embryonic kidney (HEK) 293 cells.
This is a very intriguing idea linking TRPV1-mediated calpain activation to downregulation of TRPV1! While your engineered HEK and CHO cell systems work well, can you perform this assay in more biologically relevant cells, such as DRGs, or cells more closely related to neurons, like keratinocytes, and examine endogenous proteins?
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Author response:
The following is the authors’ response to the original reviews
Reviewer #1:
While very positive towards our manuscript, this reviewer also points out three suggestions for improvement.
Overall, there are not many weaknesses. The main one I noticed is with the lipidomic analysis shown in Figs 3C, 7C, S1 and S3. While these data are an essential part of the analysis and provide strong evidence for the conclusions of the study, it is unfortunate that the methods used did not enable the distinction between two 18:1 isomers. These two isomers of 18:1 are important in C. elegans biology, because one is a substrate for FAT-2 (18:1n-9, oleic acid) and the other is not (18:1n-7, cis vaccenic acid). Although rarer in mammals, cisvaccenic acid is the most abundant fatty acid in C. elegans and is likely the most important structural MUFA. The measurement of these two isomers is not essential for the conclusions of the study, but the manuscript should include a comment about the abundance of oleic vs vaccenic acid in C. elegans (authors can find this information, even in the fat-2 mutant, in other publications of C. elegans fatty acid composition). Otherwise, readers who are not familiar with C. elegans might assume the 18:1 that is reported is likely to be mainly oleic acid, as is common in mammals.
Excellent point. As suggested by the reviewer, we now include a clarification of this in the text: "Consistent with previous publications [10], the levels of 18:1 fatty acids were greatly increased in the fat-2(wa17) mutant. It is important to note that the majority of these 18:1 fatty acids is likely 18:1n7 (vaccenic acid) and not 18:1n9 (OA) [10,23], which is the substrate of FAT-2; the lipid analysis methods used here are not able to distinguish between the two 18:1 species."
The title could be less specific; it might be confusing to readers to include the allele name in the title.
We thank the reviewer for the suggestion, and we have now modified the title:
"Forward Genetics In C. elegans Reveals Genetic Adaptations To Polyunsaturated Fatty Acid Deficiency"
There are two errors in the pathway depicted in Figure 1A. The16:0-16:1 desaturation can be performed by FAT-5, FAT-6, and FAT-7. The 18:0-18:1 desaturation can only be performed by FAT-6 and FAT-7.
We thank the reviewer for pointing out this mistake. The pathway in Fig. 1A has been corrected.
Reviewer #2:
This reviewer was also very positive towards our manuscript but also pointed out several suggestions for additional experiments or changes to the manuscript.
Major recommendations
(1) To conclude that membrane rigidification is not the major cause of defects associated with fat-2 mutations, the authors need to show that fluidity is rescued by their treatments (oleic acid or NP-40). I honestly doubt that it is the case, as oleic acid is already abundant in fat-2 mutants. It is possible that the treatments, which are effective in rescuing fluidity in paqr-2 mutants, do not have the same effects in fat-2 mutants.
The reviewer raises an important point. In an effort to address this, we have now performed a FRAP study on fat-2(wa17) mutants with/without NP40 as a fluidizing agent (with wild-type and paqr-2 mutants as controls). The new data, now included as Fig. 2J, shows that NP40 did improve the fluidity of the intestinal cell membrane in the fat-2(wa17) mutant, though not to the same degree as in the paqr-2 mutant. This is now cited in the text as follows:
"However, cultivating the fat-2(wa17) mutant in the presence of the non-ionic detergent NP40, which improves the growth of the paqr-2(tm3410) mutant [17], did not suppress the poor growth phenotype of the fat-2(wa17) mutant even though it did improve membrane fluidity as measured using FRAP (Fig. 2I-J). Similarly, supplementing the fat-2(wa17) mutant with the MUFA oleic acid (OA, 18:1), which also suppresses paqr-2(tm3410) phenotypes [17], did not suppress the poor growth phenotype of the fat-2(wa17) mutant (Fig 2K)."
(2) It is not validated experimentally that the mutations converge into FTN-2 repression. This can be verified by analyzing mRNA or protein expression of FTN-2 in the egl-9 and hif-1 mutants obtained in the screening.
Our manuscript does lean on several publications that previously established the HIF-1 pathway in C. elegans. Additionally, we now added a qPCR experiment showing that the newly isolated hif-1(et69) allele indeed suppresses the expression of ftn-2. This was an especially valuable experiment since the hif-1(et69) is proposed to act as a gain-of-function allele that would constitutively suppress ftn-2 expression. This new result is included as Fig. 6C and mentioned in the text:
"Inhibition of egl-9 promotes HIF-1 activity [41], which we here verified for the egl-9(et60) allele using western blots (Fig 6A). Additionally, we found by qPCR that ftn-2 mRNA levels are as expected reduced by the proposed gain-of-function hif-1(et69) allele (Fig 6C). We conclude that the egl-9 and hif-1 suppressor mutations likely converge on inhibiting ftn-2 and thus act similarly to the ftn-2 loss-of-function alleles."
(3) In the hif-1(et69) and ftn-2(et68) mutants, the rescues in lipid composition seem to be minor, with eicosapentaenoic acid (EPA) levels remaining low. The ftn-2 mutant data is especially concerning, as it suggests that egl-9 mutants rescue lipid composition via distinct mechanisms not including ftn-2 suppression. I suggest that the authors test the minimal doses of linoleic acid or EPA required to rescue fat-2 mutants and perform lipidomics to test which is the degree of EPA restoration that is needed. If a low level of restoration is sufficient, the hif-1 and ftn-2 mutants might indeed rescue phenotypes via a restoration of EPA levels. Otherwise, other mechanisms have to be considered.
In line with the above issue, the low level or EPA restoration in hif-1 and ftn-2 mutants raise the possibility that the mutations rescue fat-2 mutants downstream of lipid changes. The reduction in HIF-1 levels in fat-2 mutants also suggest that lipid changes affect HIF-1 expression. Thus, the "impossibility to genetically compensate PUFA deficiency" might be wrong. The above experiment would answer to this point too.
The reviewer is entirely correct to consider alternative explanations. In the lipidomics in Fig 3, we see that fat-2(wa17) worms on NGM have only ~1.5-2%mol EPA in phosphatidylcholines. When treated with 2 mM LA, the levels of EPA rise to ~10%mol, still below the ~ 25% observed in N2 but perhaps this is sufficient cause for restoring fat-2(wa17) health. Similarly, the hif-1(et69) and ftn-2(et68) mutant alleles elevate EPA levels to 5- 7% in fat-2(wa17). Thus, we have a correlation where a significant increase in EPA, obtained either through LA supplementation or through suppressor mutations (e.g. egl-9 (et60), hif-1(et69) or ftn-2(et68)), is associated with improved growth and health of the fat-2(wa17) mutant. However, correlation is of course not proof. The suggested experiment to titrate EPA to its lowest fat-2(wa17) rescuing levels and then perform lipidomics analysis was not possible in a reasonable time frame during this revision. However, preliminary experiments showed that even 25 μM LA (most of which will be converted to EPA by the worms) is enough to rescue the fat-2(wa17) or null mutant (Author response image 1), suggesting that even tiny amounts (much below the >250 μM used in our article) bring great benefits.
Author response image 1.
Nevertheless, we now acknowledge in the discussion that alternative explanations exist:
"Other mechanisms are also possible. For example, mutations in the HIF-1 pathway could somehow reduce EPA turnover rates in the fat-2(wa17) mutant and allow its levels to rise above an essential threshold. This hypothesis is consistent with the observation that the suppressors can rescue both the fat-2(wa17) mutant and fat-2 RNAi-treated worms but not the fat-2 null mutant. It is even possible, though deemed unlikely, that the fat-2(wa17) suppressors act by compensating for the PUFA shortage via some undefined separate process downstream of the lipid changes and that they only indirectly result in elevated EPA levels."
Additionally, another possible mechanism of action of the fat-2(wa17) suppressors could have been that they all cause upregulation of the FAT-2 protein. We have now explored this possibility using Western blots and found that this is an unlikely mechanism. This is presented in Fig. 6D-E and S3C-D, mentioned in the text as follows:
"We also used Western blots to evaluate the abundance of the FAT-2 protein expressed from endogenous wild-type or mutant loci but to which a HA tag was fused using CRISPR/Cas9. We found that the FAT-2::HA levels are severely reduced when the locus contains the S101F substitution present in the wa17 allele, but restored close to wild-type levels by the fat2(et65) suppressor mutation (Fig 6D-E, S3C-D Fig). The levels of FAT-2 in the HIF-1 pathway suppressors varied between experiments, with the suppressors sometimes restoring FAT-2 levels and sometimes not even when the worms were growing well (Fig 6D-E, S3C-D Fig). The fat-2(wa17) suppressors, except for the intragenic fat-2 alleles, likely do not act by increasing FAT-2 protein levels."
(4) It should be tested how Fe2+ levels are changed in the mutants, and how effective the ferric ammonium citrate treatment is. The authors might use a ftn-1::GFP reporter for this purpose.
We did obtain a strain carrying the ftn-1::GFP reporter but could not generate conclusive data with it. In particular, we saw no increase in fluorescence in fat-2(wa17) worms carrying suppressor mutations. However, we also found that even FAC treatment that rescue the fat2(wa17) mutant did not result in a measurable increased GFP levels suggesting that the reporter is not sensitive enough.
Minor comments
(1) I think that putting Figure 6A in Figure 5 would be helpful for the readers, so that they understand that the mutations converge in the same pathway.
This is now done.
(2) Page 3: While it is clear that paqr-2 regulates lipid composition, I believe that it remains unclear if it "promote the production and incorporation of PUFAs into phospholipids to restore membrane homeostasis".
A reference was missing to support that statement. Ruiz et al. (2023) is now cited for this (ref. 7).
(3) C. elegans is extremely rich in EPA (see for example DOI: 10.3390/jcm5020019), but the lipidomics data in this study rather suggest that oleic acid is predominant. I recommend to check why this discrepancy occurs.
OA (18:1n9) makes up only ~2%, but vaccenic acid (18:1n7) is ~21% in WT worms, EPA is slightly less at ~19% (Watts et al. 2002). These match with our lipidomics results although we cannot distinguish between 18:1n9 and n7. See also answer to Reviewer #1, comment 1.
(4) Abstract: The authors write that mammals do not synthesize PUFAs, which is almost correct, but they still produce the PUFA mead acid. Thus, the statement is not completely right.
Didn't know that! From literature, it is our understanding that mammals synthesize mead acid during FA deficiency but not in normal conditions, so they are not regularly producing mead acid. We have now updated the introduction:
"An exception to this exists during severe essential fatty acid deficiency when mammals can synthesize mead acid (20:3n9), though this is not a common occurrence [11]"
(5) Page 10: Eicosanoids are C20 lipid mediators, thus those produced from docosahexaenoic acid are not eicosanoids. Correct the statement.
We thank the reviewer for pointing this out. We now write:
" EPA and DHA, being long chain PUFAs should have similar fluidizing effects on membrane properties (though in vitro experiments challenge this view [78]), and both can serve as precursors of eicosanoids or docosanoids, particularly inflammatory ones [79]."
(6) Page 7: "hif-1(et69) is similarly able to suppress fat-2(wa17) when ftn-2 is knocked out" I am not sure that the data agrees with this statement, and it is unclear what we can conclude from such observation.
Fig. 2D shows that ftn-2(et68) suppresses fat-2(wa17) even in the presence of a hif-1(ok2654) null allele, showing that no HIF-1 function is required once ftn-2 is mutated. Conversely, Fig S2E shows that combining both the hif-1(et69) and the ftn-2(ok404) null allele also suppresses fat-2(wa17) (the worms do not fully reach N2 length, but they are significantly longer and were fertile adults); this is merely the expected outcome if the pathway converges on loss of ftn-2 function, though other interpretations could be possible from this experiment alone.
(7) S3 Fig: in panel B, is the last column ftn-2;egl-9 mutant? I would imagine that it is ftn2;fat-2.
We thank the reviewer for pointing this out. This has been corrected.
(8) Fig 6B, how many times has been this experiment done?
With these exact conditions (6h and 20h hypoxia) and order of strains the blot was done once, but the blot overall was done 5 times. We now added another replicate in Fig. S3A.
Note also that a few minor modifications have been made throughout the text, which can be seen in the Word file with tracked changes.
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Author response:
The following is the authors’ response to the original reviews
Public Reviews:
Reviewer #1 (Public Review):
Summary:
The manuscript by Hussain and collaborators aims at deciphering the microtubule-dependent ribbon formation in zebrafish hair cells. By using confocal imaging, pharmacology tools, and zebrafish mutants, the group of Katie Kindt convincingly demonstrated that ribbon, the organelle that concentrates glutamate-filled vesicles at the hair cell synapse, originates from the fusion of precursors that move along the microtubule network. This study goes hand in hand with a complementary paper (Voorn et al.) showing similar results in mouse hair cells.
Strengths:
This study clearly tracked the dynamics of the microtubules, and those of the microtubule-associated ribbons and demonstrated fusion ribbon events. In addition, the authors have identified the critical role of kinesin Kif1aa in the fusion events. The results are compelling and the images and movies are magnificent.
Weaknesses:
The lack of functional data regarding the role of Kif1aa. Although it is difficult to probe and interpret the behavior of zebrafish after nocodazole treatment, I wonder whether deletion of kif1aa in hair cells may result in a functional deficit that could be easily tested in zebrafish?
We have examined functional deficits in kif1aa mutants in another paper that was recently accepted: David et al. 2024. https://pubmed.ncbi.nlm.nih.gov/39373584/
In David et al., we found that in addition to a subtle role in ribbon fusion during development, Kif1aa plays a major role in enriching glutamate-filled synaptic vesicles at the presynaptic active zone of mature hair cells. In kif1aa mutants, synaptic vesicles are no longer enriched at the hair cell base, and there is a reduction in the number of synaptic vesicles associated with presynaptic ribbons. Further, we demonstrated that kif1aa mutants also have functional defects including reductions in spontaneous vesicle release (from hair cells) and evoked postsynaptic calcium responses. Behaviorally, kif1aa mutants exhibit impaired rheotaxis, indicating defects in the lateral-line system and an inability to accurately detect water flow. Because our current paper focuses on microtubule-associated ribbon movement and dynamics early in hair-cell development, we have only discussed the effects of Kif1aa directly related to ribbon dynamics during this time window. In our revision, we have referenced this recent work. Currently it is challenging to disentangle how the subtle defects in ribbon formation in kif1aa mutants contribute to the defects we observe in ribbon-synapse function.
Added to results:
“Recent work in our lab using this mutant has shown that Kif1aa is responsible for enriching glutamate-filled vesicles at the base of hair cells. In addition this work demonstrated that loss of Kif1aa results in functional defects in mature hair cells including a reduction in evoked post-synaptic calcium responses (David et al., 2024). We hypothesized that Kif1aa may also be playing an earlier role in ribbon formation.”
Impact:
The synaptogenesis in the auditory sensory cell remains still elusive. Here, this study indicates that the formation of the synaptic organelle is a dynamic process involving the fusion of presynaptic elements. This study will undoubtedly boost a new line of research aimed at identifying the specific molecular determinants that target ribbon precursors to the synapse and govern the fusion process.
Reviewer #2 (Public Review):
Summary:
In this manuscript, the authors set out to resolve a long-standing mystery in the field of sensory biology - how large, presynaptic bodies called "ribbon synapses" migrate to the basolateral end of hair cells. The ribbon synapse is found in sensory hair cells and photoreceptors, and is a critical structural feature of a readily-releasable pool of glutamate that excites postsynaptic afferent neurons. For decades, we have known these structures exist, but the mechanisms that control how ribbon synapses coalesce at the bottom of hair cells are not well understood. The authors addressed this question by leveraging the highly-tractable zebrafish lateral line neuromast, which exhibits a small number of visible hair cells, easily observed in time-lapse imaging. The approach combined genetics, pharmacological manipulations, high-resolution imaging, and careful quantifications. The manuscript commences with a developmental time course of ribbon synapse development, characterizing both immature and mature ribbon bodies (defined by position in the hair cell, apical vs. basal). Next, the authors show convincing (and frankly mesmerizing) imaging data of plus end-directed microtubule trafficking toward the basal end of the hair cells, and data highlighting the directed motion of ribbon bodies. The authors then use a series of pharmacological and genetic manipulations showing the role of microtubule stability and one particular kinesin (Kif1aa) in the transport and fusion of ribbon bodies, which is presumably a prerequisite for hair cell synaptic transmission. The data suggest that microtubules and their stability are necessary for normal numbers of mature ribbons and that Kif1aa is likely required for fusion events associated with ribbon maturation. Overall, the data provide a new and interesting story on ribbon synapse dynamics.
Strengths:
(1) The manuscript offers a comprehensive Introduction and Discussion sections that will inform generalists and specialists.
(2) The use of Airyscan imaging in living samples to view and measure microtubule and ribbon dynamics in vivo represents a strength. With rigorous quantification and thoughtful analyses, the authors generate datasets often only obtained in cultured cells or more diminutive animal models (e.g., C. elegans).
(3) The number of biological replicates and the statistical analyses are strong. The combination of pharmacology and genetic manipulations also represents strong rigor.
(4) One of the most important strengths is that the manuscript and data spur on other questions - namely, do (or how do) ribbon bodies attach to Kinesin proteins? Also, and as noted in the Discussion, do hair cell activity and subsequent intracellular calcium rises facilitate ribbon transport/fusion?
These are important strengths and as stated we are currently investigating what other kinesins and adaptors and adaptor’s transport ribbons. We have ongoing work examining how hair-cell activity impacts ribbon fusion and transport!
Weaknesses:
(1) Neither the data or the Discussion address a direct or indirect link between Kinesins and ribbon bodies. Showing Kif1aa protein in proximity to the ribbon bodies would add strength.
This is a great point. Previous immunohistochemistry work in mice demonstrated that ribbons and Kif1a colocalize in mouse hair cells (Michanski et al, 2019). Unfortunately, the antibody used in study work did not work in zebrafish. To further investigate this interaction, we also attempted to create a transgenic line expressing a fluorescently tagged Kif1aa to directly visualize its association with ribbons in vivo. At present, we were unable to detect transient expression of Kif1aa-GFP or establish a transgenic line using this approach. While we will continue to work towards understanding whether Kif1aa and ribbons colocalize in live hair cells, currently this goal is beyond the scope of this paper. In our revision we discuss this caveat.
Added to discussion:
“In addition, it will be useful to visualize these kinesins by fluorescently tagging them in live hair cells to observe whether they associate with ribbons.”
(2) Neither the data or Discussion address the functional consequences of loss of Kif1aa or ribbon transport. Presumably, both manipulations would reduce afferent excitation.
Excellent point. Please see the response above to Reviewer #1 public response weaknesses.
(3) It is unknown whether the drug treatments or genetic manipulations are specific to hair cells, so we can't know for certain whether any phenotypic defects are secondary.
This is correct and a caveat of our Kif1aa and drug experiments. In our recently published work, we confirmed that Kif1aa is expressed in hair cells and neurons, while kif1ab is present just is neurons. Therefore, it is likely that the ribbon formation defects in kif1aa mutants are restricted to hair cells. We added this expression information to our results:
“ScRNA-seq in zebrafish has demonstrated widespread co-expression of kif1ab and kif1aa mRNA in the nervous system. Additionally, both scRNA-seq and fluorescent in situ hybridization have revealed that pLL hair cells exclusively express kif1aa mRNA (David et al., 2024; Lush et al., 2019; Sur et al., 2023).”
Non-hair cell effects are a real concern in our pharmacology experiments. To mitigate this in our pharmacological experiments, we have performed drug treatments at 3 different timescales: long-term (overnight), short-term (4 hr) and fast (30 min) treatments. The fast experiments were done after 30 min nocodazole drug treatment, and after this treatment we observed reduced directional motion and fusions. This fast drug treatment should not incur any long-term changes or developmental defects as hair-cell development occurs over 12-16 hrs. However, we acknowledge that drug treatments could have secondary phenotypic effects or effects that are not hair-cell specific. In our revision, we discuss these issues.
Added to discussion:
“Another important consideration is the potential off-target effects of nocodazole. Even at non-cytotoxic doses, nocodazole toxicity may impact ribbons and synapses independently of its effects on microtubules. While this is less of a concern in the short- and medium-term experiments (30-70 min and 4 hr), long-term treatments (16 hrs) could introduce confounding effects. Additionally, nocodazole treatment is not hair cell-specific and could disrupt microtubule organization within afferent terminals as well. Thus, the reduction in ribbon-synapse formation following prolonged nocodazole treatment may result from microtubule disruption in hair cells, afferent terminals, or a combination of the two.”
Reviewer #3 (Public Review):
Summary:
The manuscript uses live imaging to study the role of microtubules in the movement of ribeye aggregates in neuromast hair cells in zebrafish. The main findings are that
(1) Ribeye aggregates, assumed to be ribbon precursors, move in a directed motion toward the active zone;
(2) Disruption of microtubules and kif1aa increases the number of ribeye aggregates and decreases the number of mature synapses.
The evidence for point 2 is compelling, while the evidence for point 1 is less convincing. In particular, the directed motion conclusion is dependent upon fitting of mean squared displacement that can be prone to error and variance to do stochasticity, which is not accounted for in the analysis. Only a small subset of the aggregates meet this criteria and one wonders whether the focus on this subset misses the bigger picture of what is happening with the majority of spots.
Strengths:
(1) The effects of Kif1aa removal and nocodozole on ribbon precursor number and size are convincing and novel.
(2) The live imaging of Ribeye aggregate dynamics provides interesting insight into ribbon formation. The movies showing the fusion of ribeye spots are convincing and the demonstrated effects of nocodozole and kif1aa removal on the frequency of these events is novel.
(3) The effect of nocodozole and kif1aa removal on precursor fusion is novel and interesting.
(4) The quality of the data is extremely high and the results are interesting.
Weaknesses:
(1) To image ribeye aggregates, the investigators overexpressed Ribeye-a TAGRFP under the control of a MyoVI promoter. While it is understandable why they chose to do the experiments this way, expression is not under the same transcriptional regulation as the native protein, and some caution is warranted in drawing some conclusions. For example, the reduction in the number of puncta with maturity may partially reflect the regulation of the MyoVI promoter with hair cell maturity. Similarly, it is unknown whether overexpression has the potential to saturate binding sites (for example motors), which could influence mobility.
We agree that overexpression of transgenes under using a non-endogenous promoter in transgenic lines is an important consideration. Ideally, we would do these experiments with endogenously expressed fluorescent proteins under a native promoter. However, this was not technically possible for us. The decrease in precursors is likely not due to regulation by the myo6a promoter. Although the myo6a promoter comes on early in hair cell development, the promoter only gets stronger as the hair cells mature. This would lead to a continued increase rather than a decrease in puncta numbers with development.
Protein tags such as tagRFP always have the caveat of impacting protein function. This is in partly why we complemented our live imaging with analyses in fixed tissue without transgenes (kif1aa mutants and nocodazole/taxol treatments).
In our revision, we did perform an immunolabel on myo6b:riba-tagRFP transgenic fish and found that Riba-tagRFP expression did not impact ribbon synapse numbers or ribbon size. This analysis argues that the transgene is expressed at a level that does not impact ribbon synapses. This data is summarized in Figure 1-S1.
Added to the results:
“Although this latter transgene expresses Riba-TagRFP under a non-endogenous promoter, neither the tag nor the promoter ultimately impacts cell numbers, synapse counts, or ribbon size (Figure 1-S1A-E).”
Added to methods:
“Tg(myo6b:ctbp2a-TagRFP)<sup>idc11Tg</sup> reliably labels mature ribbons, similar to a pan-CTBP immunolabel at 5 dpf (Figure 1-S1B). This transgenic line does not alter the number of hair cells or complete synapses per hair cell (Figure 1-S1A-D). In addition, myo6b:ctbp2a-TagRFP does not alter the size of ribbons (Figure 1-S1E).”
(2) The examples of punctae colocalizing with microtubules look clear (Figures 1 F-G), but the presentation is anecdotal. It would be better and more informative, if quantified.
We did attempt a co-localization analysis between microtubules and ribbons but did not move forward with it due to several issues:
(1) Hair cells have an extremely crowded environment, especially since the nucleus occupies the majority of the cell. All proteins are pushed together in the small space surrounding the nucleus and ultimately, we found that co-localization analyses were not meaningful because the distances were too small.
(2) We also attempted to segment microtubules in these images and quantify how many ribbons were associated with microtubules, but 3D microtubule segmentation was not accurate in hair cells due to highly varying filament intensities, filament dynamics and the presence of diffuse cytoplasmic tubulin signal.
Because of these challenges we concluded the best evidence of ribbon-microtubule association is through visualization of ribbons and their association with microtubules over time (in our timelapses). We see that ribbons localize to microtubules in all our timelapses, including the examples shown (Movies S2-S10). The only instance of ribbon dissociation it when ribbons switch from one filament to another. We did not observe free-floating ribbons in our study.
(3) It appears that any directed transport may be rare. Simply having an alpha >1 is not sufficient to declare movement to be directed (motor-driven transport typically has an alpha approaching 2). Due to the randomness of a random walk and errors in fits in imperfect data will yield some spread in movement driven by Brownian motion. Many of the tracks in Figure 3H look as though they might be reasonably fit by a straight line (i.e. alpha = 1).
(4) The "directed motion" shown here does not really resemble motor-driven transport observed in other systems (axonal transport, for example) even in the subset that has been picked out as examples here. While the role of microtubules and kif1aa in synapse maturation is strong, it seems likely that this role may be something non-canonical (which would be interesting).
Yes, it is true, that directed transport of ribbon precursors is relatively rare. Only a small subset of the ribbon precursors moves directionally (α > 1, 20 %) or have a displacement distance > 1 µm (36 %) during the time windows we are imaging. The majority of the ribbons are stationary. To emphasize this result we have added bar graphs to Figure 3I,K to illustrate this result and state the numbers behind this result more clearly.
“Upon quantification, 20.2 % of ribbon tracks show α > 1, indicative of directional motion, but the majority of ribbon tracks (79.8 %) show α < 1, indicating confinement on microtubules (Figure 3I, n = 10 neuromasts, 40 hair cells, and 203 tracks).
To provide a more comprehensive analysis of precursor movement, we also examined displacement distance (Figure 3J). Here, as an additional measure of directed motion, we calculated the percent of tracks with a cumulative displacement > 1 µm. We found 35.6 % of tracks had a displacement > 1 µm (Figure 3K; n = 10 neuromasts, 40 hair cells, and 203 tracks).”
We cannot say for certain what is happening with the stationary ribbons, but our hypothesis is that these ribbons eventually exhibit directed motion sufficient to reach the active zone. This idea is supported by the fact that we see ribbons that are stationary begin movement, and ribbons that are moving come to a stop during the acquisition of our timelapses (Movies S4 and S5). It is possible that ribbons that are stationary may not have enough motors attached, or there may be a ‘seeding’ phase where Ribeye aggregates are condensing on the ribbon.
We also reexamined our MSD a values as the a values we observed in hair cells were lower than those seen canonical motor-driven transport (where a approaches 2). One reason for this difference may arise from the dynamic microtubule network in developing hair cells, which could affect directional ribbon movement. In our revision we plotted the distribution of a values which confirmed that in control hair cells, the majority of the a values we see are typically less than 2 (Figure 7-S1A). Interestingly we also compared the distribution a values between control and taxol-treated hair cells, where the microtubule network is more stable, and found that the distribution shifted towards higher a values (Figure 7-S1A). We also plotted only ‘directional’ tracks (with a > 1) and observed significantly higher a values in taxol-treated hair cells (Figure 7-S1B). This is an interesting result which indicates that although the proportion of directional tracks (with a > 1) is not significantly different between control and taxol-treated hair cells (which could be limited by the number of motor/adapter proteins), the ribbons that move directionally do so with greater velocities when the microtubules are more stable. This supports our idea that the stability of the microtubule network could be why ribbon movement does not resemble canonical motor transport. This analysis is presented as a new figure (Figure 7-S1A-B) and is referred to in the text in the results and the discussion.
Results:
“Interestingly, when we examined the distribution of α values, we observed that taxol treatment shifted the overall distribution towards higher α a values (Figure 7-S1A). In addition, when we plotted only tracks with directional motion (α > 1), we found significantly higher α values in hair cells treated with taxol compared to controls (Figure 7-S1B). This indicates that in taxol-treated hair cells, where the microtubule network is stabilized, ribbons with directional motion have higher velocities.”
Discussion:
“Our findings indicate that ribbons and precursors show directed motion indicative of motor-mediated transport (Figure 3 and 7). While a subset of ribbons moves directionally with α values > 1, canonical motor-driven transport in other systems, such as axonal transport, can achieve even higher α values approaching 2 (Bellotti et al., 2021; Corradi et al., 2020). We suggest that relatively lower α values arise from the highly dynamic nature of microtubules in hair cells. In axons, microtubules form stable, linear tracks that allow kinesins to transport cargo with high velocity. In contrast, the microtubule network in hair cells is highly dynamic, particularly near the cell base. Within a single time frame (50-100 s), we observe continuous movement and branching of these networks. This dynamic behavior adds complexity to ribbon motion, leading to frequent stalling, filament switching, and reversals in direction. As a result, ribbon transport appears less directional than the movement of traditional motor cargoes along stable axonal filaments, resulting in lower α values compared to canonical motor-mediated transport. Notably, treatment with taxol, which stabilizes microtubules, increased α values to levels closer to those observed in canonical motor-driven transport (Figure 7-S1). This finding supports the idea that the relatively lower α values in hair cells are a consequence of a more dynamic microtubule network. Overall, this dynamic network gives rise to a slower, non-canonical mode of transport.”
(5) The effect of acute treatment with nocodozole on microtubules in movie 7 and Figure 6 is not obvious to me and it is clear that whatever effect it has on microtubules is incomplete.
When using nocodazole, we worked to optimize the concentration of the drug to minimize cytotoxicity, while still being effective. While the more stable filaments at the cell apex remain largely intact after nocodazole treatment, there are almost no filaments at the hair cell base, which is different from the wild-type hair cells. In addition, nocodazole-treated hair cells have more cytoplasmic YFP-tubulin signal compared to wild type. We have clarified this in our results. To better illustrate the effect of nocodazole and taxol we have also added additional side-view images of hair cells expressing YFP-tubulin (Figure 4-S1F-G), that highlight cytoplasmic YFP-tubulin and long, stabilized microtubules after 3-4 hr treatment with nocodazole and taxol respectively. In these images we also point out microtubules at the apical region of hair cells that are very stable and do not completely destabilize with nocodazole treatment at concentrations that are tolerable to hair cells.
“We verified the effectiveness of our in vivo pharmacological treatments using either 500 nM nocodazole or 25 µM taxol by imaging microtubule dynamics in pLL hair cells (myo6b:YFP-tubulin). After a 30-min pharmacological treatment, we used Airyscan confocal microscopy to acquire timelapses of YFP-tubulin (3 µm z-stacks, every 50-100 s for 30-70 min, Movie S8). Compared to controls, 500 nM nocodazole destabilized microtubules (presence of depolymerized YFP-tubulin in the cytosol, see arrows in Figure 4-S1F-G) and 25 µM taxol dramatically stabilized microtubules (indicated by long, rigid microtubules, see arrowheads in Figure 4-S1F,H) in pLL hair cells. We did still observe a subset of apical microtubules after nocodazole treatment, indicating that this population is particularly stable (see asterisks in Figure 4-S1F-H).”
To further address concerns about verifying the efficacy of nocodazole and taxol treatment on microtubules, we added a quantification of our immunostaining data comparing the mean acetylated-a-tubulin intensities between control, nocodazole and taxol-treated hair cells. Our results show that nocodazole treatment reduces the mean acetylated-a-tubulin intensity in hair cells. This is included as a new figure (Figure 4-S1D-E) and this result is referred to in the text. To better illustrate the effect of nocodazole and taxol we have also added additional side-view images of hair cells after overnight treatment with nocodazole and taxol (Figure 4-S1A-C).
“After a 16-hr treatment with 250 nM nocodazole we observed a decrease in acetylated-a-tubulin label (qualitative examples: Figure 4A,C, Figure 4-S1A-B). Quantification revealed significantly less mean acetylated-a-tubulin label in hair cells after nocodazole treatment (Figure 4-S1D). Less acetylated-a-tubulin label indicates that our nocodazole treatment successfully destabilized microtubules.”
“Qualitatively more acetylated-a-tubulin label was observed after treatment, indicating that our taxol treatment successfully stabilized microtubules (qualitative examples: Figure 4-S1A,C). Quantification revealed an overall increase in mean acetylated-a-tubulin label in hair cells after taxol treatment, but this increase did not reach significance (Figure 4-S1E).”
Recommendations for the authors:
Reviewer #1 (Recommendations For The Authors):
(1) The manuscript is fairly dense. For instance, some information is repeated (page 3 ribbon synapses form along a condensed timeline in zebrafish hair cells: 12-18 hrs, and on .page 5. These hair cells form 3-4 ribbon synapses in just 12-18 hrs). Perhaps, the authors could condense some of the ideas? The introduction could be shortened.
We have eliminated this repeated text in our revision. We have shortened the introduction 1275 to 1038 words (with references)
(2) The mechanosensory structure on page 5 is not defined for readers outside the field.
Great point, we have added addition information to define this structure in the results:
“We staged hair cells based on the development of the apical, mechanosensory hair bundle. The hair bundle is composed of actin-based stereocilia and a tubulin-based kinocilium. We used the height of the kinocilium (see schematic in Figure 1B), the tallest part of the hair bundle, to estimate the developmental stage of hair cells as described previously…”
(3) Figure 1E is quite interesting but I'd rather show Figure S1 B/C as they provide statistics. In addition, the authors define 4 stages : early, intermediate, late, and mature for counting but provide only 3 panels for representative examples by mixing late/mature.
We were torn about which ribbon quantification graph to show. Ultimately, we decided to keep the summary data in Figure 1E. This is primarily because the supplementary Figure will be adjacent to the main Figure in the Elife format, and the statistics will be easy to find and view.
Figure 1 now provides a representative image for both late and mature hair cells.
(4.) The ribbon that jumps from one microtubule to another one is eye-catching. Can the authors provide any statistics on this (e.g. percentage)?
Good point. In our revision, we have added quantification for these events. We observe 2.8 switching events per neuromast during our fast timelapses. This information is now in the text and is also shown in a graph in Figure 3-S1D.
“Third, we often observed that precursors switched association between neighboring microtubules (2.8 switching events per neuromast, n= 10 neuromasts; Figure 3-S1C-D, Movie S7).”
(5) With regard to acetyl-a-tub immunocytochemistry, I would suggest obtaining a profile of the fluorescence intensity on a horizontal plane (at the apical part and at the base).
(6) Same issue with microtubule destruction by nocodazole. Can the authors provide fluorescence intensity measurements to convince readers of microtubule disruption for long and short-term application.
Regarding quantification of microtubule disruption using nocodazole and taxol. We did attempt to create profiles of the acetylated tubulin or YFP-tubulin label along horizontal planes at the apex and base, but the amount variability among cells and the angle of the cell in the images made this type of display and quantification challenging. In our revision we as stated above in our response to Reviewer #1’s public comment, we have added representative side-view images to show the disruptions to microtubules more clearly after short and long-term drug experiments (Figure 4-S1A-C, F-H). In addition, we quantified the reduction in acetylated tubulin label after overnight treatment with nocodazole and found the signal was significantly reduced (Figure 3-S1D-E). Unfortunately, we were unable to do a similar quantification due to the variability in YFP-tubulin intensity due to variations in mounting. The following text has been added to the results:
“Quantification revealed significantly less mean acetylated-a-tubulin label in hair cells after nocodazole treatment (Figure 4-S1D).”
“Quantification revealed an overall increase in mean acetylated-a-tubulin label in hair cells after taxol treatment, but this increase did not reach significance (Figure 4-S1A,C,E).”
(7) It is a bit difficult to understand that the long-term (overnight) microtubule destabilization leads to a reduction in the number of synapses (Figure 4F) whereas short-term (30 min) microtubule destabilization leads to the opposite phenotype with an increased number of ribbons (Figure 6G). Are these ribbons still synaptic in short-term experiments? What is the size of the ribbons in the short-term experiments? Alternatively, could the reduction in synapse number upon long-term application of nocodazole be a side-effect of the toxicity within the hair cell?
Agreed-this is a bit confusing. In our revision, we have changed our analyses, so the comparisons are more similar between the short- and long-term experiments–we examined the number of ribbons and precursor per cells (apical and basal) in both experiments (Changed the panel in Figure 4G, Figure 4-S2G and Figure 5G). In our live experiments we cannot be sure that ribbons are synaptic as we do not have a postsynaptic co-label. Also, we are unable to reliably quantify ribbon and precursor size in our live images due to variability in mounting. We have changed the text to clarify as follows:
Results:
“In each developing cell, we quantified the total number of Riba-TagRFP puncta (apical and basal) before and after each treatment. In our control samples we observed on average no change in the number of Riba-TagRFP puncta per cell (Figure 6G). Interestingly, we observed that nocodazole treatment led to a significant increase in the total number of Riba-TagRFP puncta after 3-4 hrs (Figure 6G). This result is similar to our overnight nocodazole experiments in fixed samples, where we also observed an increase in the number of ribbons and precursors per hair cell. In contrast to our 3-4 hr nocodazole treatment, similar to controls, taxol treatment did not alter the total number of Riba-TagRFP puncta over 3-4 hrs (Figure 6G). Overall, our overnight and 3-4 hr pharmacology experiments demonstrate that microtubule destabilization has a more significant impact on ribbon numbers compared to microtubule stabilization.”
Discussion:
“Ribbons and microtubules may interact during development to promote fusion, to form larger ribbons. Disrupting microtubules could interfere with this process, preventing ribbon maturation. Consistent with this, short-term (3-4 hr) and long-term (overnight) nocodazole increased ribbon and precursor numbers (Figure 6AG; Figure 4G), suggesting reduced fusion. Long-term treatment (overnight) resulted in a shift toward smaller ribbons (Figure 4H-I), and ultimately fewer complete synapses (Figure 4F).”
Nocodazole toxicity: in response to Reviewer # 2’s public comment we have added the following text in our discussion:
Discussion:
“Another important consideration is the potential off-target effects of nocodazole. Even at non-cytotoxic doses, nocodazole toxicity may impact ribbons and synapses independently of its effects on microtubules. While this is less of a concern in the short- and medium-term experiments (30 min to 4 hr), long-term treatments (16 hrs) could introduce confounding effects. Additionally, nocodazole treatment is not hair cell-specific and could disrupt microtubule organization within afferent terminals as well. Thus, the reduction in ribbon-synapse formation following prolonged nocodazole treatment may result from microtubule disruption in hair cells, afferent terminals, or a combination of the two.”
(8) Does ribbon motion depend on size or location?
It is challenging to reliability quantify the actual area of precursors in our live samples, as there is variability in mounting and precursors are quite small. But we did examine the location of ribbon precursors (using tracks > 1 µm as these tracks can easily be linked to cell location in Imaris) with motion in the cell. We found evidence of ribbons with tracks > 1 µm throughout the cell, both above and below the nucleus. This is now plotted in Figure 3M. We have also added the following test to the results:
“In addition, we examined the location of precursors within the cell that exhibited displacements > 1 µm. We found that 38.9 % of these tracks were located above the nucleus, while 61.1 % were located below the nucleus (Figure 3M).”
Although this is not an area or size measurement, this result suggests that both smaller precursors that are more apical, and larger precursors/ribbons that are more basal all show motion.
(9) The fusion event needs to be analyzed in further detail: when one ribbon precursor fuses with another one, is there an increase in size or intensity (this should follow the law of mass conservation)? This is important to support the abstract sentence "ribbon precursors can fuse together on microtubules to form larger ribbons".
As mentioned above it is challenging accurately estimate the absolute size or intensity of ribbon precursors in our live preparation. But we did examine whether there is a relative increase in area after ribbon fuse. We have plotted the change in area (within the same samples) for the two fusion events in shown in Figure 8-S1A-B. In these examples, the area of the puncta after fusion is larger than either of the two precursors that fuse. Although the areas are not additive, these plots do provide some evidence that fusion does act to form larger ribbons. To accompany these plots, we have added the following text to the results:
“Although we could not accurately measure the areas of precursors before and after fusion, we observed that the relative area resulting from the fusion of two smaller precursors was greater than that of either precursor alone. This increase in area suggests that precursor fusion may serve as a mechanism for generating larger ribbons (see examples: Figure 8-S1A-B).”
Because we were unable to provide more accurate evidence of precursor fusion resulting in larger ribbons, we have removed this statement from our abstract and lessened our claims elsewhere in the manuscript.
(10) The title in Figure 8 is a bit confusing. If fusion events reflect ribbon precursors fusion, it is obvious it depends on ribbon precursors. I'd like to replace this title with something like "microtubules and kif1aa are required for fusion events"
We have changed the figure title as suggested, good idea.
Reviewer #2 (Recommendations For The Authors):
(1) Figure 1C. The purple/magenta colors are hard to distinguish.
We have made the magenta color much lighter in the Figure 1C to make it easier to distinguish purple and magenta.
(2) There are places where some words are unnecessarily hyphenated. Examples: live-imaging and hair-cell in the abstract, time-course in the results.
In our revision, we have done our best to remove unnecessary hyphens, including the ones pointed out here.
(3) Figure 4H and elsewhere - what is "area of Ribeye puncta?" Related, I think, in the Discussion the authors refer to "ribbon volume" on line 484. But they never measured ribbon volume so this needs to be clarified.
We have done best to clarify what is meant by area of Ribeye puncta in the results and the methods:
Results:
“We also observed that the average of individual Ribeyeb puncta (from 2D max-projected images) was significantly reduced compared to controls (Figure 4H). Further, the relative frequency of individual Ribeyeb puncta with smaller areas was higher in nocodazole treated hair cells compared to controls (Figure 4I).”
Methods:
“To quantify the area of each ribbon and precursor, images were processed in a FIJI ‘IJMacro_AIRYSCAN_simple3dSeg_ribbons only.ijm’ as previously described (Wong et al., 2019). Here each Airyscan z-stack was max-projected. A threshold was applied to each image, followed by segmentation to delineate individual Ribeyeb/CTBP puncta. The watershed function was used to separate adjacent puncta. A list of 2D objects of individual ROIs (minimum size filter of 0.002 μm2) was created to measure the 2D areas of each Ribeyeb/CTBP puncta.”
We did refer to ribbon volume once in the discussion, but volume is not reflected in our analyses, so we have removed this mention of volume.
(4) More validation data showing gene/protein removal for the crispants would be helpful.
Great suggestion. As this is a relatively new method, we have created a figure that outlines how we genotype each individual crispant animal analyzed in our study Figure 6-S1. In the methods we have also added the following information:
“fPCR fragments were run on a genetic analyzer (Applied Biosystems, 3500XL) using LIZ500 (Applied Biosystems, 4322682) as a dye standard. Analysis of this fPCR revealed an average peak height of 4740 a.u. in wild type, and an average peak height of 126 a.u. in kif1aa F0 crispants (Figure 6-S1). Any kif1aa F0 crispant without robust genomic cutting or a peak height > 500 a.u. was not included in our analyses.”
Reviewer #3 (Recommendations For The Authors):
Lines 208-209--should refer to the movie in the text.
Movie S1 is now referenced here.
It would be helpful if the authors could analyze and quantify the effect of nocodozole and taxol on microtubules (movie 7).
See responses above to Reviewer #1’s similar request.
Figure 7 caption says "500 mM" nocodozole.
Thank you, we have changed the caption to 500 nM.
One problem with the MSD analysis is that it is dependent upon fits of individual tracks that lead to inaccuracies in assigning diffusive, restricted, and directed motion. The authors might be able to get around these problems by looking at the ensemble averages of all the tracks and seeing how they change with the various treatments. Even if the effect is on a subset of ribeye spots, it would be reassuring to see significant effects that did not rely upon fitting.
We are hesitant to average the MSD tracks as not all tracks have the same number of time steps (ribbon moving in and out of the z-stack during the timelapse). This makes it challenging for us to look at the ensembles of all averages accurately, especially for the duration of the timelapse. This is the main reason why added another analysis, displacements > 1µm as another readout of directional motion, a measure that does not rely upon fitting.
The abstract states that directed movement is toward the synapse. The only real evidence for this is a statement in the results: "Of the tracks that showed directional motion, while the majority move to the cell base, we found that 21.2 % of ribbon tracks moved apically." A clearer demonstration of this would be to do the analysis of Figure 2G for the ribeye aggregates.
If was not possible to do the same analysis to ribbon tracks that we did for the EB3-GFP analysis in Figure 2. In Figure 2 we did a 2D tracking analysis and measured the relative angles in 2D. In contrast, the ribbon tracking was done in 3D in Imaris not possible to get angles in the same way. Further the MSD analysis was outside of Imaris, making it extremely difficult to link ribbon trajectories to the 3D cellular landscape in Imaris. Instead, we examined the direction of the 3D vectors in Imaris with tracks > 1µm and determined the direction of the motion (apical, basal or undetermined). For clarity, this data is now included as a bar graph in Figure 3L. In our results, we have clarified the results of this analysis:
“To provide a more comprehensive analysis of precursor movement, we also examined displacement distance (Figure 3J). Here, as an additional measure of directed motion, we calculated the percent of tracks with a cumulative displacement > 1 µm. We found 35.6 % of tracks had a displacement > 1 µm (Figure 3K; n = 10 neuromasts, 40 hair cells and 203 tracks). Of the tracks with displacement > 1 µm, the majority of ribbon tracks (45.8 %) moved to the cell base, but we also found a subset of ribbon tracks (20.8 %) that moved apically (33.4 % moved in an undetermined direction) (Figure 3L).”
Some more detail about the F0 crispants should be provided. In particular, what degree of cutting was observed and what was the criteria for robust cutting?
See our response to Reviewer 2 and the newly created Figure 6-S1.
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www.biorxiv.org www.biorxiv.org
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Author Response
The following is the authors’ response to the original reviews.
Reviewer #1 (Public Review):
Several concerns are raised from the current study.
1) Previous studies showed that iTregs generated in vitro from culturing naïve T cells with TGF-b are intrinsically unstable and prone to losing Foxp3 expression due to lack of DNA demethylation in the enhancer region of the Foxp3 locus (Polansky JK et al, Eur J Immunol., 2008, PMID: 18493985). It is known that removing TGF-b from the culture media leads to rapid loss of Foxp3 expression. In the current study, TGF-b was not added to the media during iTreg restimulation, therefore, the primary cause for iTreg instability should be the lack of the positive signal provided by TGF-b. NFAT signal is secondary at best in this culturing condition.
In restimulation, void of TGFb is necessary to cause iTreg instability. Otherwise, the setup is similar to the iTreg-inducing environment (Author response image 1). On the other hand, the ultimate goal of this study is to provide a scenario that bears some resemblance of clinical treatment, where TGFb may not be available. The reviewer is correct in stating that TGFb is essential for iTreg stability, we are studying the role played by NFAT in iTreg instability in vitro, and possibly in potential clinical use of iTreg .
Author response image 1.
Restimulation with TGFb will persist iTreg inducing environment, resulting in less pronounced instability. Sorted Foxp3-GFP+ iTregs were rested for 1d, and then rested or restimulated in the presence of TGF-β for 2 d. Percentages of Foxp3+ cells were analyzed by intracellular staining of Foxp3 after 2 d.
2) It is not clear whether the NFAT pathway is unique in accelerating the loss of Foxp3 expression upon iTreg restimulation. It is also possible that enhancing T cell activation in general could promote iTreg instability. The authors could explore blocking T cell activation by inhibiting other critical pathways, such as NF-kb and c-Jun/c-Fos, to see if a similar effect could be achieved compared to CsA treatment.
We thank the reviewer for this suggestion. We performed this experiment according to see extent of the role that NFAT plays, or whether other major pathways are involved. As Author response image 2 shows, solely inhibiting NFAT effectively rescued the instability of iTreg. The inhibition of NFkB (BAY 11-7082), c-Jun (SP600125), or a c-Jun/c-Fos complex (T5224) had no discernable effect, or in one case, possibly further reduction in stability. These results may indicate that NFAT plays a crucial and special role in TCR activation, which leads to iTreg instability. Other pathways, as far as how this experiment is designed, do not appear to be significantly involved.
Author response image 2.
Comparing effects of NFAT, NF-kB and c-Jun/c-Fos inhibitors on iTreg instability. Sorted Foxp3-GFP+ iTregs were rested for 1d, then restimulated by anti-CD3 and CD28 in the presence of listed inhibitors. Percentages of Foxp3+ cells were analyzed by intracellular staining after 2d restimulation.
3) The authors linked chromatin accessibility and increased expression of T helper cell genes to the loss of Foxp3 expression and iTreg instability. However, it is not clear how the former can lead to the latter. It is also not clear whether NFAT binds directly to the Foxp3 locus in the restimulated iTregs and inhibits Foxp3 expression.
T helper gene activation is likely to cause instability in iTregs by secreting more inflammatory cytokines, as shown in Figure Q9, for example, IL-21 secretion. Further investigation is needed to understand how these genes contribute to Foxp3 gene instability exactly. With our limited insight, there may be two possibilities. 1. IL-21 directly affects Foxp3 through its impact on certain inflammation-related transcription factors (TFs). 2. There could be an indirect relationship where NFAT has a greater tendency to bind to those inflammatory TFs when iTreg instability appears, promoting the upregulation of these Th genes like in activated T cells, while being less likely to bind to SMAD and Foxp3, representing a competitive behavior. We at the moment cannot comprehend the intricacies that lead to the differential effects on T helper genes and Treg related genes.
With that said, we have previously attempted to explore the direct effect of NFAT on Foxp3 gene locus. Foxp3 transcription in iTregs primarily relies on histone modifications such as H3K4me3 (Tone et al., 2008; Lu et al., 2011) rather than DNA demethylation (Ohkura et al., 2012; Hilbrands et al., 2016). Previous studies have reported that NFAT and SMAD3 can together promote the histone acetylation of Foxp3 genes (Tone et al., 2008). In our previous set of experiments, we simultaneously obtained information of NFAT binding sites and H3K4me3. In Foxp3 locus, we observed a decreasing trend in NFAT binding to the CNS3 region of Foxp3 in restimulated iTregs compared to resting iTregs (Author response image 3). Additionally, the H3K4me3 modification in the CNS3 region of Foxp3 decreased upon iTreg restimulation, but inhibiting NFAT nuclear translocation with CsA could maintain this modification at its original level (Author response image 3).
Author response image 3.
The NFAT binding and histone modification on Foxp3 gene locus. Genome track visualization of NFAT binding profiles and H3K4me3 profiles in Foxp3 CNS3 locus in two batches of dataset.
Based on these preliminary explorations, it is concluded that NFAT can directly bind to the Foxp3 locus, and it appears that NFAT decreases upon restimulation, resulting in a decrease in H3K4me3, ultimately leading to the close association of NFAT and Foxp3 instability. However, due to limited sample replicates, these data need to be verified for more solid conclusions. We speculate that during the induction of iTregs, NFAT may recruit histone-modifying enzymes to open the Foxp3 CNS3 region, and this effect is synergistic with SMAD. When instability occurs upon restimulation, NFAT binding to Foxp3 weakens due to the absence of SMAD's assistance, subsequently reducing the recruitment of histone modifications enzyme and ultimately inhibiting Foxp3 transcription.
Reviewer #2 (Public Review):
(1) Some concerns about data processing and statistic analysis.
The authors did not provide sufficient information on statistical data analysis; e.g. lack of detailed descriptions about
-the precise numbers of technical/biological replicates of each experiment
-the method of how the authors analyze data of multiple comparisons... Student t-test alone is generally insufficient to compare multiple groups; e.g. figure 1.
These inappropriate data handlings are ruining the evidence level of the precious findings.
We thank the reviewer for pointing out this important aspect. In the figure legend, numbers of independently-performed experiment repeats are shown as N, biological replicates of each experiment as n. Student’s t test was used for comparing statistical significance between two groups. In this manuscript, all calculations of significant differences were based on comparisons between two groups. There were no multiple conditions compared simultaneously within a single group, and thus, no other calculation methods were used.
(2) Untransparent data production; e.g. the method of Motif enrichment analysis was not provided. Thus, we should wait for the author's correction to fully evaluate the significance and reliability of the present study.
Per this reviewer’s request, we have provided detailed descriptions of the data analysis for Fig 5, including both the method section and the Figure legend, as presented below:
“The peaks annotations were performed with the “annotatePeak” function in the R package ChIPseeker (Yu et al, 2015).
The plot of Cut&Tag signals over a set of genomic regions were calculated by using “computeMatrix” function in deepTools and plotted by using “plotHeatmap” and “plotProfile” functions in deepTools. The motif enrichment analysis was performed by using the "findMotifsGenome.pl" command in HOMER with default parameters.
The motif occurrences in each peak were identified by using FIMO (MEME suite v5.0.4) with the following settings: a first-order Markov background model, a P value cutoff of 10-4, and PWMs from the mouse HOCOMOCO motif database (v11).”
Additionally, we have also supplemented the method section with further details on the analysis of RNA-seq and ATAC-seq data.
(3) Lack of evidence in human cells. I wonder whether human PBMC-derived iTreg cells are similarly regulated.
This is a rather complicated issue, human T cells express FoxP3 upon TCR stimulation (PNAS, 103(17): 6659–6664), whose function is likely to protect T cells from activation induced cell death, and does not offer Treg like properties. In contrast in mice, FoxP3 can be used as an indicator of Treg. Currently, this is not a definitive marker for Treg in human, our FoxP3 based readouts do not apply. Nevertheless, we have now investigated whether inhibiting calcium signaling or NFAT could enhance the stability of human iTreg. As shown in Author response image 4, we found that the proportion of Foxp3-expressing cells did not show significant changes across the different conditions, while the MFI analysis revealed that CsA-treated iTreg exhibited higher Foxp3 expression levels compared to both restimulated iTreg and rest iTreg. However, CM4620 had no significant effect on Foxp3 stability, consistent with the observation of its limited efficacy in suppressing human iTreg long term activation. In summary, our results suggest that inhibiting NFAT signaling through CsA treatment can help maintain higher levels of Foxp3 expression in human iTreg.
Author response image 4.
Effect of inhibiting NFAT and calcium on human iTreg stability. Human naïve CD4 cells from PBMC were subjected to a two-week induction process to generate human iTreg. Subsequently, human iTreg were restimulated for 2 days with dynabeads followed by 2 days of rest in the prescence of CsA and CM-4620. Four days later, percentages of Foxp3+ cells and Foxp3 mean fluorescence intensity (MFI) were analyzed by intracellular staining.
(4) NFAT regulation did not explain all of the differences between iTregs and nTregs, as the authors mentioned as a limitation. Also, it is still an open question whether NFAT can directly modulate the chromatin configuration on the effector-type gene loci, or whether NFAT exploits pre-existing open chromatin due to the incomplete conversion of Treg-type chromatin landscape in iTreg cells. The authors did not fully demonstrate that the distinct pattern of chromatin regional accessibility found in iTreg cells is the direct cause of an effector-type gene expression.
To our surprise, the inhibition of NFkB (BAY 11-7082), c-Jun (SP600125), and the c-Jun/c-Fos complex (T5224) resulted in minimal alterations, as shown in Fig Q1. This seems to argue that NFAT may play a more special role in events leading iTreg instability.
We hypothesize that NFAT takes advantage of pre-existing open chromatin state due to the incomplete conversion of chromatin landscape in iTreg cells. Because iTreg cells, after induction, already exhibit inherent chromatin instability, with highly-open inflammatory genes. Furthermore, when iTreg cells were restimulated, the subsequent change in chromatin accessibility was relatively limited and not rescued by NFAT inhibitor treatment (Author response image 5). Therefore, in the case of iTreg cells, we propose that NFAT exploits the easy access of those inflammatory genes, leading to rapid destabilization of iTreg cells in the short term.
In contrast, tTreg cells possess a relatively stable chromatin structure in the beginning, it would be interesting to investigate whether NFAT or calcium signaling could disrupt chromatin accessibility during the activation or expansion of tTreg cells. It is possible that NFAT might cause the loss of the originally established demethylation map and open up inflammatory loci, thereby inducing a shift in gene transcriptional profiles, equally leading to instability.
Author response image 5.
Chromatin accessibility of Rest, Retimulated, CsA/ORAIinh treated restimulated iTreg. PCA visualization of chromatin accessibility profiles of different cell types. Color indicates cell type.
To establish a direct relationship between gene locus accessibility and its overexpression, a controlled experimental approach can be employed. One such method involves precise manipulation of the accessibility of a specific genomic locus using CRISPR-mediated epigenetic modifications at targeted loci. Subsequently, the impact of this manipulation on the expression level of the target gene can be precisely examined. By conducting these experiments, it will be possible to determine whether the augmented gene accessibility directly causes the observed gene overexpression.
Reviewer #1 (Recommendations For The Authors):
1) It might be helpful to add TGF-b to the iTreg restimulation culture to remove the influence of the lack of TGF-b from the equation, and measure the influence of SOCE/NFAT on iTreg instability.
Please refer to Author response image 1.
2) Alternatively, authors can also culture iTreg cells with TGF-b for 2 weeks when they undergo epigenetic changes and become more stabilized (Polansky JK et al, Eur J Immunol., 2008, PMID: 18493985). At this point, the stabilized iTregs can be used to measure the influence of SOCE/NFAT on iTreg instability.
In the study conducted by Polansky, it was observed in Figure 1 that prolonged exposure to TGF-β fails to induce stable Foxp3 expression and demethylation of the Treg-specific demethylated region (TSDR). Based on this finding, we could consider exploring alternative approaches to obtain a more stabilized iTreg population. One such approach could be isolating Foxp3+helios-Nrp1- iTreg cells directly from the peripheral in vivo, which are also known as pTregs. Generally, pTreg cells generated in vivo tend to be more stable compared to iTreg cells induced in vitro, and they already exhibit partial demethylation of the Treg signature, as shown in Fig 6C (Polansky JK et al, Eur J Immunol., 2008, PMID: 18493985). Investigating the role of NFAT and calcium signaling in pTreg cells would provide further insights into the additional roles of NFAT in Treg phenotypical transitions, particularly its role in chromatin accessibility.
3) In Figure 3, NFAT binding to the inflammatory genes in iTreg cells was even stronger than in activated T conventional cells. This is possibly due to Tconv cells being stimulated only once while iTregs were restimulated. A fair comparison should be conducted with restimulated activated conventional T cells.
Figure 3 demonstrates the accessibility of inflammatory gene loci, rather than NFAT binding. Comparing restimulated Tconvs with restimulated iTreg cells is indeed a valuable suggestion, as their activation state and polarization in iTreg directions could lead to distinct chromatin accessibility. Although one is activated long term regularly and the other is activated long term under iTreg polarization, it is highly likely that the chromatin state of both activated Tconvs and iTreg cells is highly open, especially in terms of the accessibility of inflammatory genes. This may provide us with a new perspective to understand iTreg cells, but will unlikely affect our central conclusion.
4) In the in vivo experiment in Figure 6, a control condition without OVA immunization should be included as a baseline.
We have performed this experiment in the absence of OVA, as depicted in Author response image 6. In the absence of OVA immunization, both WT-ORAI and DN-ORAI iTreg exhibited substantial stability, although DN-ORAI demonstrated a slightly less stable trend. Upon activation with 40ug and 100ug of OVA, DN-ORAI iTreg demonstrated enhanced stability than WT-ORAI iTreg, maintaining a higher proportion of Foxp3 expression.
Author response image 6.
Stability of DN-ORAI iTreg in vivo with or without OVA immunization. WT-ORAI/DN-ORAI-GFP+-transfected CD45.2+ Foxp3-RFP+ OT-II iTregs were transferred i.v. into CD45.1 mice. Recipients were left or immunized with OVA323-339 in Alum adjuvant. On day 5, mLN were harvested and analyzed for Foxp3 expression by intracellular staining.
Reviewer #2 (Recommendations For The Authors):
Major
Some concerns about the data processing and statistic analysis, as mentioned in the public review. In the figure legend, what does it mean e.g. n=3, N=3? Technical triplicate experiments? Three mice? Independently-performed three experiments? The authors should define it at least in the "Statistical analysis" in the method section otherwise the readers cannot determine the reason why they mainly use SEM for the data description.
Moreover, in some cases, the number of experiments was not sure; e.g., Fig.1B, Fig. 5.
How did the authors analyze data including multiple comparisons? Student t-test alone is generally insufficient to compare multiple groups; e.g. figure 1.
We thank the reviewer for pointing out this omission. Now, in the figure legend, numbers of independently-performed experiment repeats are shown as N, biological replicates of each experiment as n. For Fig. 1B, N=2, and for Fig 5, we have acquired NFAT Cut&Tag data for 2 times, N=2. Student’s t test was used for comparing statistical significance between two groups. In this manuscript, all calculations of significant differences were based on comparisons between two groups. There were no multiple conditions compared simultaneously within a single group, and thus, no other calculation methods were involved apart from the Student's t-test.
In Figure 1A, the difference in suppressiveness seemed subtle. Data collection of multiple doses of Tconv:Treg ratio will enhance the reliability of such kind of analysis.
We have now attempted the suppression assay with varying Treg:Tconv ratios and observed that the suppressive effect of iTreg was more obvious than that of tTreg when co-cultured at a 1:1 ratio with Tconv cells. However, as the cell number of tTreg and iTreg decreased, the inhibitory effects converged.
Author response image 7.
Compare multiple dose of Tconv:Treg ratio in suppression function CFSE-labelled OT-II T cells were stimulated with OVA-pulsed DC, then different number of Foxp3-GFP+ iTregs and tTregs were added to the culture to suppress the OT-II proliferation. After 4 days, CFSE dilution were analyzed. Left, Representative histograms of CFSE in divided Tconvs. Right, graph for the percentage of divided Tconvs.
In Figure 3F, to which group did the shaded peaks belong? In this context, the authors should focus on "Activation Region" peaks (open chromatin signature in both TcAct & iTreg defined in Fig. 4D) but I did not find the peak in the focusing DNA regions in TcAct (e.g. the shaded regions in IL-4 loci). The clear attribution of the peaks to the heatmap will enhance the visibility and understanding of readers.
We have selected some typical peaks that belong to Fig 3D. These genes encompass some T-cell activation-associated transcription factors, such as Irf4, Atf3, as well as multiple members of the Tnf family including Lta, Tnfsf4, Tnfsf8, and Tnfsf14. Additionally, genes related to inflammation such as Il12rb2, Il9, and Gzmc are included. These genes show elevated accessibility upon T-cell activation, partially open in activated nTreg cells, referred to as the "Activation Region." They collectively exhibit high accessibility in iTreg cells, which may contribute to their instability.
Author response image 8.
Chromatin accessibility of some “Activation Region”. Genomic track showing chromatin accessibility of Irf4, Atf3, Lta, Tnfsf8, Tnfsf4, Tnsfsf14, Il12rb2, Il9, Gzmc in activated Tconv and iTreg.
In Figure 4A/S4A, the information on cell death will help the understanding of readers because the sustained SOCE is associated with cell survival as shown in Fig. S2. The authors can discuss the relationships between cell death and Foxp3 retention, which potentially leads to a further interesting question; e.g. the selective/resistance to activation-induced cell death as the identity of Treg cells.
As shown in Author response image 9, activated iTreg cells indeed exhibit a certain degree of cell death compared to resting iTreg cells. The inhibition of NFAT by CsA enhances the survival rate of iTreg cells, but the inhibition of ORAI by CM-4620 leads to more severe cell death. The cell death induced by CsA and CM-4620 is not consistent, indicating that there may not be a direct proportional relationship between cell death and the expression of Foxp3 and Treg identity.
Author response image 9.
Relationship of cell death and Foxp3 stability in restimulated iTregs. Sorted Foxp3-GFP+ iTregs were rested for 1d, then restimulated by anti-CD3 and CD28 in the presence of CsA or CM-4620. After 2d restimulation, live cell percentage were analyzed by staining of Live/Dead fixable Aqua, and percentages of Foxp3+ cells were analyzed by intracellular staining of Foxp3. Upper, live cell percentage of iTregs. Lower, percentages of Foxp3 in iTregs.
In Figure 5, the information for the data interpretation was insufficient.
We have provided detailed descriptions of the data analysis for Fig 5, including both the method section and the Figure legend, as presented below:
“The peaks annotations were performed with the “annotatePeak” function in the R package ChIPseeker (Yu et al, 2015). The plot of Cut&Tag signals over a set of genomic regions were calculated by using “computeMatrix” function in deepTools and plotted by using “plotHeatmap” and “plotProfile” functions in deepTools. The motif enrichment analysis was performed by using the "findMotifsGenome.pl" command in HOMER with default parameters. The motif occurrences in each peak were identified by using FIMO (MEME suite v5.0.4) with the following settings: a first-order Markov background model, a P value cutoff of 10-4, and PWMs from the mouse HOCOMOCO motif database (v11).”
Additionally, we have also supplemented the method section with further details on the analysis of RNA-seq and ATAC-seq data.
The correlation between the open chromatin status of the gene loci described in Fig.5E and the expression at mRNA level? e.g.; Do iTreg-Act cells produce a higher level of IL-21 than nTreg-act? The analysis in Fig.5F-G should be performed in parallel with nTreg cells to emphasize the distinct NFAT-chromatin regulation in iTreg cells.
We have now compared the secretion levels of IL-21 in tTreg and iTreg upon activation and treated with CsA by ELISA. As shown in Author response image 10, tTreg did not secrete IL-21 regardless of activation status (undetectable), while iTreg did not secrete IL-21 at resting state but exhibited IL-21 secretion after 48 h of activation. Moreover, the secretion of IL-21 was inhibited by CsA and CM-4620 treatment. This observation aligns with our earlier findings where we observed nuclear binding of NFAT to gene loci of these cytokines, enhancing their expression and pushing iTreg unstable under inflammatory conditions. These findings further underscore the likelihood that the inhibition of calcium and NFAT signaling might contribute to the stabilization of iTreg by suppressing the secretion of inflammatory cytokines.
Author response image 10.
IL-21 secretion in tTreg and iTreg upon activation. iTregs and tTregs were sorted and restimulated with anti-CD3 and anti-CD28 antibodies, in the presence of CsA and CM-4620. Cell culture supernatant were harvested after 2 d restimulation and IL-21 secretion was analyzed by ELISA.
Performing a parallel comparison of NFAT activity between tTreg and iTreg cells was initially part of our experimental plan. However, it proved challenging in practice, as we encountered difficulties in efficiently infecting tTreg cells with NFAT-flag. Consequently, we could not obtain a sufficient number of tTreg cells for conducting Cut&Tag experiments.
Based on our observations, we speculate that there might be substantial differences in the accessibility of genes in tTreg cells, leading to considerable variations in the repertoire of genes available for NFAT to regulate. As a result, we expect significant differences in the nuclear localization and activity of NFAT between iTreg and tTreg cells.
In Figure 6C, what does the FCM plot between Foxp3-CFSE look like?
The authors can discuss the mechanism of ORAI-DN-mediated through such analysis; e.g. the possibility that selective proliferation defect by ORAI-DN in Foxp3- cells led to an increased percentage of Foxp3, not only just unstable transcription of Foxp3.
This is an in vitro experiment to assess the suppressive effect of iTreg on Tconv proliferation. Therefore, CFSE is used to stain Tconv cells, but not iTreg cells, so we did not detect proliferation feature of iTreg.
Minor
Confusing terminology of "tTreg" at line 47, etc. "natural Treg" contains both thymic-derived Treg and periphery-derived Treg cells. (A Abbas et al. Nat Immunol. 2013)
We have now changed the designation to tTreg at line 47. tTreg refers to thymus-derived regulatory T cells, while nTreg includes both tTreg and pTreg. However, it is important to note that the Treg cells used in our study were isolated from the spleen of 2-4-month-old Foxp3-GFP or Foxp3-RFP mice. The CD4+ T cells were first enriched using the CD4 Isolation kit, and the FACSAriaII was utilized to collect CD4+ Foxp3-GFP/RFP+ Treg cells. Subsequently, Helios and Nrp-1 staining revealed that the majority of these cells were nTreg, with only approximately 6% being pTreg. Overall, we consider the cells we used as tTreg.
In all FCM analyses, the authors should clarify how to detect Foxp3 expression; Foxp3-GFP/Foxp3-RFP/Intracellular staining like Figure S5A (but not specified in the other FCM plots)
All Foxp3 expressions in the article were assessed using intracellular staining, as described in the methods section, and we have added specific descriptions to each figure legend. The reason for employing intracellular staining is that we used Foxp3-IRES-GFP mice, where GFP and Foxp3 are not fused into a single protein, existing as separate proteins after expression. Therefore, during induction, the appearance of GFP protein might potentially represent the presence of Foxp3. However, in cases of Foxp3 instability, the degradation of GFP protein may not be entirely synchronized with that of Foxp3 protein, making GFP an unreliable indicator of Foxp3 expression levels. As a result, for the purification of pure iTreg cells, we used Foxp3-GFP/RFP fluorescence, while for observing instability, we employed intranuclear staining of Foxp3.
In Figure 6B, the captions were lacking in the two graphs on the right side
The two restimulation conditions, 0.125+0.25 and 0.25+0.5, have been added into Fig 6B right side.
In Figure S2, the annotation of the x-y axis was missing.
Added.
Lack of reference at line 292.
Reference 42-46 were added.
In the method section, the authors should note the further product information of antibodies and reagents to enhance reproducibility and transparency. Making a list that clarifies the suppliers, Ab clone, product IDs, etc. is encouraged. The authors did not specify the supplier of recombinant proteins and which type of TGF-beta (TGF-beta 1, 2, or 3?).
A detailed description of the mice, antibodies, Peptide recombinant protein, commercial kit, and software has been provided and incorporated into the methods section.
In the method section, the authors should clarify which Foxp3-reporter strain. There are many strains of Foxp3-reporter mice in the world. In line 373, is the "FoxP3-IRES-GFP transgenic mice" true? Knock-in strain or BAC-transgene?
This mouse is a gift from Hai Qi Lab in Tsinghua University. They acquired this mouse strain from Jackson Laboratory, and the strain name is B6.Cg-Foxp3tm2Tch/J, Strain #:006772. An IRES-EGFP-SV40 poly A sequence was inserted immediately downstream of the endogenous Foxp3 translational stop codon, but upstream of the endogenous polyA signal, generating a bicistronic locus encoding both Foxp3 and EGFP.
The age of mice used in the experiments should be specified, and confusing words such as "young" should not be used in any method descriptions; e.g. line 405.
The detailed mouse age has been added in the methods section. “To prepare Tconv, tTreg and iTreg for experiments, spleen was isolated from 2-4-month-old Foxp3-GFP mice for Tconv and tTreg sorting, and 6-week-old mice for iTreg induction.”
The method of how the original ATAC-seq/Cut & Tag data were generated was not described in the method section.
Added in method section.
The reference section was incomplete, and the style was not unified. e.g.; ref 7, 24, 25, 26 ... I gave up checking all.
The style of ref 7, 22, 24, 26, 28, 31, 33, 35 were modified.
Changes in manuscript:
Author Name: “Huiyun Lv” to “Huiyun Lyu”.
Fig 1A was updated according to Reviwer 2’s suggestion.
Fig S3E and associated description was added according to Reviwer 2’s suggestion.
Fig S4C and associated description was added according to Reviwer 1’s suggestion.
Fig 5H and associated description was added according to Reviwer 2’s suggestion.
Fig 6D were updated according to Reviwer 1’s suggestion.
Fig 2D was corrected, the labels for gapdh and actin in the iTreg panel were inadvertently switched. The mistake has been rectified, and the original gel image will be provided.
Fig 2A and Fig 4A was updated.
The style of Fig 6B and Fig S2A was modified.
Method:
Mice: FoxP3-IRES-GFP with more description.
Flow Cytometry sorting and FACS: the detailed mouse age has been added. RNA-seq analysis, ATAC-sequencing, ATAC-seq analysis, Cut&Tag assay, Cut&Tag data analysis: more description was added.
Statistical analysis: “Numbers of independently-performed experiment repeats are shown as N, biological replicates of each experiment as n.” were added.
Reference: Ref 42-46 and 49-52 were added. The style of ref 7, 22, 24, 26, 28, 31, 33, 35 were corrected.
A detailed description of the mice, antibodies, Peptide recombinant protein, commercial kit, and software has been provided.
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Author response:
The following is the authors’ response to the original reviews.
Public Reviews:
Reviewer #1 (Public Review):
Summary:
In their manuscript, Yu et al. describe the chemotactic gradient formation for CCL5 bound to - i.e. released from - glycosaminoglycans. The authors provide evidence for phase separation as the driving mechanism behind chemotactic gradient formation. A conclusion towards a general principle behind the finding cannot be drawn since the work focuses on one chemokine only, which is particularly prone to glycan-induced oligomerisation.
Strengths:
The principle of phase separation as a driving force behind and thus as an analytical tool for investigating protein interactions with strongly charged biomolecules was originally introduced for protein-nucleic acid interactions. Yu et al. have applied this in their work for the first time for chemokine-heparan sulfate interactions. This opens a novel way to investigate chemokine-glycosaminoglycan interactions in general.
Response: Thanks for the encouragement of the reviewer.
Weaknesses:
As mentioned above, one of the weaknesses of the current work is the exemplification of the phase separation principle by applying it only to CCL5-heparan sulfate interactions. CCL5 is known to form higher oligomers/aggregates in the presence of glycosaminoglycans, much more than other chemokines. It would therefore have been very interesting to see, if similar results in vitro, in situ, and in vivo could have been obtained by other chemokines of the same class (e.g. CCL2) or another class (like CXCL8).
Response: We share the reviewer’s opinion that to investigate more molecules/cytokines that interact with heparan sulfate in the system should be of interesting. We expect that researchers in the field will adapt the concept to continue the studies on additional molecules. Nevertheless, our earlier study has demonstrated that bFGF was enriched to its receptor and triggered signaling transduction through phase separation with heparan sulfate (PMID: 35236856; doi: 10.1038/s41467-022-28765-z), which supports the concept that phase separation with heparan sulfate on the cell surface may be a common mechanism for heparan sulfate binding proteins. The comment of the reviewer that phase separation is related to oligomerization is demonstrated in (Figure 1—figure supplement 2C and D), showing that the more easily aggregated mutant, A22K-CCL5, does not undergo phase separation.
In addition, the authors have used variously labelled CCL5 (like with the organic dye Cy3 or with EGFP) for various reasons (detection and immobilisation). In the view of this reviewer, it would have been necessary to show that all the labelled chemokines yield identical/similar molecular characteristics as the unlabelled wildtype chemokine (such as heparan sulfate binding and chemotaxis). It is well known that labelling proteins either by chemical tags or by fusion to GFPs can lead to manifestly different molecular and functional characteristics.
Response: We agree with the reviewer that labeling may lead to altered property of a protein, thus, we have compared chemotactic activity of CCL5 and CCL5-EGFP (Figure 2—figure supplement 1). To further verify this, we performed additional experiment to compare chemotactic activity between CCL5 and Cy3-CCL5 (see Author response image 1). For the convenience of readers, we have combined the original Figure 2—figure supplement 1 with the new data (Figure R1), which replaced original Figure 2—figure supplement 1.
Author response image 1.
Chemotactic function of CCL5-EGFP and CCL5-Cy3. Cy3-Labeled CCL5 has similar activity as CCL5, 50 nM CCL5 or CCL5-Cy3 were added to the lower chamber of the Transwell. THP-1 cells were added to upper chambers. Data are mean ± s.d. n=3. P values were determined by unpaired two-tailed t-tests. NS, Not Significant.
Reviewer #2 (Public Review):
Although the study by Xiaolin Yu et al is largely limited to in vitro data, the results of this study convincingly improve our current understanding of leukocyte migration.
(1) The conclusions of the paper are mostly supported by the data although some clarification is warranted concerning the exact CCL5 forms (without or with a fluorescent label or His-tag) and amounts/concentrations that were used in the individual experiments. This is important since it is known that modification of CCL5 at the N-terminus affects the interactions of CCL5 with the GPCRs CCR1, CCR3, and CCR5 and random labeling using monosuccinimidyl esters (as done by the authors with Cy-3) is targeting lysines. Since lysines are important for the GAG-binding properties of CCL5, knowledge of the number and location of the Cy-3 labels on CCL5 is important information for the interpretation of the experimental results with the fluorescently labeled CCL5. Was the His-tag attached to the N- or C-terminus of CCL5? Indicate this for each individual experiment and consider/discuss also potential effects of the modifications on CCL5 in the results and discussion sections.
Response: We agree with the reviewer that labeling may lead to altered property of a protein, thus, we have compared chemotactic activity of CCL5 and CCL5-EGFP (Figure 2—figure supplement 1). To further verify this, we performed additional experiment to compare chemotactic activity between CCL5 and Cy3-CCL5 (see Author response image 1). For the convenience of readers, we have combined the original Figure 2—figure supplement 1 with the new data (Author response image 1), which replaced original Figure 2—figure supplement 1.
The His-tag is attached to the C-terminus of CCL5, in consideration of the potential impact on the N-terminus.
(2) In general, the authors appear to use high concentrations of CCL5 in their experiments. The reason for this is not clear. Is it because of the effects of the labels on the activity of the protein? In most biological tests (e.g. chemotaxis assays), unmodified CCL5 is active already at low nM concentrations.
Response: We agree with the reviewer that the CCL5 concentrations used in our experiments were higher than reported chemotaxis assays and also higher than physiological levels in normal human plasma. In fact, we have performed experiments with lower concentration of CCL5, where the effect of LLPS was not seen though the chemotactic activity of the cytokine was detected. Thus, LLPS-associated chemotactic activity may represent a scenario of acute inflammatory condition when the inflammatory cytokines can increase significantly.
(3) For the statistical analyses of the results, the authors use t-tests. Was it confirmed that data follow a normal distribution prior to using the t-test? If not a non-parametric test should be used and it may affect the conclusions of some experiments.
Response: We thank the reviewer for pointing out this issue. As shown in Author response table 1, The Shapiro-Wilk normality test showed that only two control groups (CCL5 and 44AANA47-CCL5+CHO K1) in Figure 3 did not conform to the normal distribution. The error was caused by using microculture to count and calculate when there were very few cells in the microculture. For these two groups, we re-counted 100 μL culture medium to calculate the number of cells. The results were consistent with the positive distribution and significantly different from the experimental group (Author response image 3). The original data for the number of cells chemoattractant by 500 nM CCL5 was revised from 0, 247, 247 to 247, 123, 370 and 500 nM 44AANA47 +CHO-K1 was revised from 1111, 1111, 98 to 740, 494, 617. The revised data does not affect the conclusion.
Author response table 1.
Table R1 Shapiro-Wilk test results of statistical data in the manuscript
Author response image 3.
Quantification of THP-1collected from the lower chamber. Data are mean ± s.d. n=3. P values were determined by unpaired two-tailed t-tests.
Recommendations for the authors:
Reviewer #1:
See the weaknesses section of the Public Review. In addition, the authors should discuss the X-ray structure of CCL5 in complex with a heparin disaccharide in comparison with their docked structure of CCL5 and a heparin tetrasaccharide.
Response: Our study, in fact, is strongly influenced by the report (Shaw, Johnson et al., 2004) that heparin disaccharide interaction with CCL5, which is highlighted in the text (page5, line100-102).
Reviewer #2:
(1) Clearly indicate in the results section and figure legends (also for the supplementary figures) which form and concentration of CCL5 is used.
Response: The relevant missing information is indicated across the manuscript.
(2) Clearly indicate which GAG was used. Was it heparin or heparan sulfate and what was the length (e.g. average molecular mass if known) or source (company?)?
Response: Relevant information is added in the section “Materials and Methods.
(3) Line 181: What do you mean exactly with "tiny amounts"?
Response: “tiny amounts” means 400 transfected cells. This is described in the section of Materials and Methods. It is now also indicated in the text and legend to the figure.
(4) Lines 216-217: This is a very general statement without a link to the presented data. No combination of chemokines is used, in vivo testing is limited (and I agree very difficult). You may consider deleting this sentence (certainly as an opening sentence for the Discussion).
Response: We appreciate very much for the thoughtful suggestion of the reviewer. This sentence is deleted in the revised manuscript.
(5) Why was 5h used for the in vitro chemotaxis assay? This is extremely long for an assay with THP-1 cells.
Response: We apologize for the unclear description. The 5 hr includes 1 hr pre- incubation of CCL5 with the cells enable to form phase separation. After transferring the cells into the upper chamber, the actual chemotactic assay was 4 hr. This is clarified in the Materials and Methods section and the legend to each figure.
(6) Define "Sec" in Sec-CCL5-EGFP and "Dil" in the legend of Figure 4.
Response: The Sec-CCL5-EGFP should be “CCL5-EGFP’’, which has now been corrected. Dil is a cell membrane red fluorescent probe, which is now defined.
(7) Why are different cell concentrations used in the experiment described in Figure 5?
Response: The samples were from three volunteers who exhibited substantially different concentrations of cells in the blood. The experiment was designed using same amount of blood, so we did not normalize the number of the cell used for the experiment. Regardless of the difference in cell numbers, all three samples showed the same trend.
(8) Check the text for some typos: examples are on line 83 "ratio of CCL5"; line 142 "established cell lines"; line 196 "peripheral blood mononuclear cells"; line 224 "to mediate"; line 226 "bind"; line 247 "to form a gradient"; line 248 "of the glycocalyx"; line 343 and 346 "tetrasaccharide"; line 409-410 "wild-type"; line 543 "on the surface of CHO-K1 and CHO-677"; line 568 "white".
Response: Thanks for the careful reading. The typo errors are corrected and Manuscript was carefully read by colleagues.
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Reviewer #3 (Public review):
Summary
This work investigated the immune response in the murine retina after focal laser lesions. These lesions are made with close to 2 orders of magnitude lower laser power than the more prevalent choroidal neovascularization model of laser ablation. Histology and OCT together show that the laser insult is localized to the photoreceptors and spares the inner retina, the vasculature and the pigment epithelium. As early as 1-day after injury, a loss of cell bodies in the outer nuclear layer is observed. This is accompanied by strong microglial proliferation to the site of injury in the outer retina where microglia do not typically reside. The injury did not seem to result in the extravasation of neutrophils from the capillary network, constituting one of the main findings of the paper. The demonstrated paradigm of studying the immune response and potentially retinal remodeling in the future in vivo is valuable and would appeal to a broad audience in visual neuroscience.
Strengths
Adaptive optics imaging of murine retina is cutting edge and enables non-destructive visualization of fluorescently labeled cells in the milieu of retinal injury. As may be obvious, this in vivo approach is a benefit for studying fast and dynamic immune processes on a local time scale - minutes and hours, and also for the longer days-to-months follow-up of retinal remodeling as demonstrated in the article. In certain cases, the in vivo findings are corroborated with histology.
The analysis is sound and accompanied by stunning video and static imagery. A few different sets of mouse models are used: a) two different mouse lines, each with a fluorescent tag for neutrophils and microglia, b) two different models of inflammation - endotoxin-induced uveitis (EAU) and laser ablation are used to study differences in the immune interaction.
One of the major advances in this article is the development of the laser ablation model for 'mild' retinal damage as an alternative to the more severe neovascularization models. This model would potentially allow for controlling the size, depth and severity of the laser injury opening interesting avenues for future study.
The time-course, 2D and 3D spatial activation pattern of microglial activation are striking and provide an unprecedented view of the retinal response to mild injury.
Editor's note: The authors have addressed all the previous concerns raised by the reviewers.
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Author response:
The following is the authors’ response to the previous reviews
Public Reviews:
Reviewer #2 (Public review):
Summary:
This study uses in vivo multimodal high-resolution imaging to track how microglia and neutrophils respond to light-induced retinal injury from soon after injury to 2 months post-injury. The in vivo imaging finding was subsequently verified by ex vivo study. The results suggest that despite the highly active microglia at the injury site, neutrophils were not recruited in response to acute light-induced retinal injury.
Strengths:
An extremely thorough examination of the cellular-level immune activity at the injury site. In vivo imaging observations being verified using ex vivo techniques is a strong plus.
Thank you!
Weaknesses:
This paper is extremely long, and in the perspective of this reviewer, needs to be better organized. Update: Modifications have been made throughout, which has made the manuscript easier to follow.
Thank you!
Study weakness: though the finding prompts more questions and future studies, the findings discussed in this paper is potentially important for us to understand how the immune cells respond differently to different severity level of injury. The study also demonstrated an imaging technology which may help us better understand cellular activity in living tissue during earlier time points.
We agree that AOSLO has much to offer and this represents some of the earliest reports of its kind.
Comments on revisions:
I appreciate the thorough clarification and re-organization by the authors, and the messages in the manuscript are now more apparent. I recommend also briefly discussing limitations/future improvements in the discussion or conclusion.
We have added a section to the discussion entitled “Limitations and future improvements”, please see lines 665 – 677.
Reviewer #3 (Public review):
Summary
This work investigated the immune response in the murine retina after focal laser lesions. These lesions are made with close to 2 orders of magnitude lower laser power than the more prevalent choroidal neovascularization model of laser ablation. Histology and OCT together show that the laser insult is localized to the photoreceptors and spares the inner retina, the vasculature and the pigment epithelium. As early as 1-day after injury, a loss of cell bodies in the outer nuclear layer is observed. This is accompanied by strong microglial proliferation to the site of injury in the outer retina where microglia do not typically reside. The injury did not seem to result in the extravasation of neutrophils from the capillary network, constituting one of the main findings of the paper. The demonstrated paradigm of studying the immune response and potentially retinal remodeling in the future in vivo is valuable and would appeal to a broad audience in visual neuroscience.
Strengths
Adaptive optics imaging of murine retina is cutting edge and enables non-destructive visualization of fluorescently labeled cells in the milieu of retinal injury. As may be obvious, this in vivo approach is a benefit for studying fast and dynamic immune processes on a local time scale - minutes and hours, and also for the longer days-to-months follow-up of retinal remodeling as demonstrated in the article. In certain cases, the in vivo findings are corroborated with histology.
Thank you!
The analysis is sound and accompanied by stunning video and static imagery. A few different sets of mouse models are used, a) two different mouse lines, each with a fluorescent tag for neutrophils and microglia, b) two different models of inflammation - endotoxin-induced uveitis (EAU) and laser ablation are used to study differences in the immune interaction.
Thank you!
One of the major advances in this article is the development of the laser ablation model for 'mild' retinal damage as an alternative to the more severe neovascularization models. This model would potentially allow for controlling the size, depth and severity of the laser injury opening interesting avenues for future study.
Thank you!
The time-course, 2D and 3D spatial activation pattern of microglial activation are striking and provide an unprecedented view of the retinal response to mild injury.
We agree that this more complete spatial and temporal evaluation made possible by in vivo imaging is novel.
Weaknesses
Generalization of the (lack of) neutrophil response to photoreceptor loss - there is ample evidence in literature that neutrophils are heavily recruited in response to severe retinal damage that includes photoreceptor loss. Why the same was not observed here in this article remains an open question. One could hypothesize that neutrophil recruitment might indeed occur under conditions that are more in line with the more extreme damage models, for example, with a stronger and global ablation (substantially more photoreceptor loss over a larger area). This parameter space is unwieldy and sufficiently large to address the question conclusively in the current article, i.e. how much photoreceptor loss leads to neutrophil recruitment? By the same token, the strong and general conclusion in the title - Photoreceptor loss does not recruit neutrophils - cannot be made until an exhaustive exploration be made of the same parameter space. A scaling back may help here, to reflect the specific, mild form of laser damage explored here, for instance - Mild photoreceptor loss does not recruit neutrophils despite...
We are striving for clarity and accuracy in our title without adding too many qualifiers. At present, we feel that the title as submitted is consistent and aligned with the central finding of our manuscript. The nuance that the reviewer points to is elaborated in the body of the manuscript and we hope the general readership appreciates the same level of detail as appreciated by reviewer #3.
EIU model - The EIU model was used as a positive control for neutrophil extravasation. Prior work with flow cytometry has shown a substantial increase in neutrophil counts in the EIU model. Yet, in all, the entire article shows exactly 2 examples in vivo and 3 ex vivo (Figure 7) of extravasated neutrophils from the EIU model (n = 2 mice). The general conclusion made about neutrophil recruitment (or lack thereof) is built partly upon this positive control experiment. But these limited examples, especially in the case where literature reports a preponderance of extravasated neutrophils, raise a question on the paradigm(s) used to evaluate this effect in the mild laser damage model.
This is a helpful suggestion. We agree that readers should see more evidence of the positive control. Therefore we have now included two more supplementary files that show that there is a strong neutrophil response to EIU. In Figure 7 – supplementary figure 1, we show many Ly-6G-positive neutrophils in the retina seen with histology at the 24 hour time point. In Figure 7 – video 3, we show massive Catchup-positive neutrophil presence in vivo at 24hrs as well. This aligns with our positive control and also the literature.
Overall, the strengths outweigh the weaknesses, provided the conclusions/interpretations are reconsidered.
With the added clarification about the magnitude of the neutrophil response in EIU, we feel that the conclusions presented in the manuscript as-is are valid and appropriate.
Recommendations for the authors:
Reviewer #3 (Recommendations for the authors):
The authors are applauded for embracing the reviewers' feedback and making substantial revisions. Some minor comments below:
The weakness noted in the public review encourages the authors to reconsider the interpretations drawn based on the results. One would have expected to see far more examples of extravasated neutrophils from the EIU model. That this was not seen weakens the neutrophil recruitment claim substantially. Even without this claim, the methods, laser damage model, time-course and spatial activation pattern of microglial activation are all striking and unprecedented. So, as stated in the public review, the strengths do indeed outweigh the weaknesses once the neutrophil claim is softened.
We address this in the response above. A strong neutrophil response was observed to EIU. This was confirmed with both histology and in vivo imaging.
This was alluded to by Reviewer 1 in the prior review - at times, there is an overemphasis on imaging technology that distracts from the scientific questions. The imaging is undoubtedly cutting-edge but also documented in prior work by the authors. Any efforts to reduce or balance the emphasis would help with the general flow.
Given that these discoveries are made possible partly through new technology, we prefer to keep the details of the innovation in the current manuscript. Given the exceptionally large readership of eLife, we feel some description of the AOSLO imaging is warranted in the manuscript.
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Author response:
The following is the authors’ response to the original reviews
Reviewer 1 (Public review):
Summary:
Gene transfer agent (GTA) from Bartonella is a fascinating chimeric GTA that evolved from the domestication of two phages. Not much is known about how the expression of the BaGTA is regulated. In this manuscript, Korotaev et al noted the structural similarity between BrrG (a protein encoded by the ror locus of BaGTA) to a well-known transcriptional anti-termination factor, 21Q, from phage P21. This sparked the investigation into the possibility that BaGTA cluster is also regulated by anti-termination. Using a suite of cell biology, genetics, and genome-wide techniques (ChIP-seq), Korotaev et al convincingly showed that this is most likely the case. The findings offer the first insight into the regulation of GTA cluster (and GTA-mediated gene transfer) particularly in this pathogen Bartonella. Note that anti-termination is a well-known/studied mechanism of transcriptional control. Anti-termination is a very common mechanism for gene expression control of prophages, phages, bacterial gene clusters, and other GTAs, so in this sense, the impact of the findings in this study here is limited to Bartonella.
Strengths:
Convincing results that overall support the main claim of the manuscript.
Weaknesses:
A few important controls are missing.
We sincerely appreciate reviewer #1's positive assessment of our manuscript. In response to the concern regarding control samples/experiments, we have addressed this issue in our revision, by providing data of the replicates of our experiments. We acknowledge that antitermination is a well-established mechanism of expression control in bacteria, including bacterial gene clusters, phages, prophages, and at least one other GTA. As reviewer #2 also noted, our study presents a unique example of phage co-domestication, where antitermination integrates both phage remnants at the regulatory level. We have emphasized this original aspect more clearly in the revised manuscript.
Reviewer 1 (Recommendations for the authors):
(1) Provide Rsmd and DALI scores to show how similar the AlphaFold-predicted structures of BrrG are to other anti-termination factors. This should be done for Fig1B and also for Suppl. Fig 1 to support the claim that BrrG, GafA, GafZ, Q21 share structural features.
In the revised manuscript we provide Rsmd and DALI scores in the supplementary Fig. 1A (Suppl. Fig. 1A). In Suppl. Fig. 1B we further include a heatmap of similiarity values.
(2) Throughout the manuscript, flow cytometry data of gfp expression was used and shown as single replicate. Korotaev et al wrote in the legends that error bars are shown (that is not true for e.g. Figs. 3, 4, and 5). It is difficult for reviewers/readers to gauge how reliable are their experiments.
In the revised manuscript we show all replicates for the flow cytometry histograms.
For Fig. 2C, all replicates are provided in Suppl. Fig. 3.
For Fig. 3B, all replicates are provided in Suppl. Fig. 4.
For Fig. 4B, all replicates are provided in Suppl. Fig. 5.
For Fig. 5B, all replicates are provided in Suppl. Fig. 6.
(3) I am unsure how ChIP-seq in Fig. 2A was performed (with anti-FLAG or anti-HA antibodies? I cannot tell from the Materials & Methods). More importantly, I did not see the control for this ChIP-seq experiment. If a FLAG-tagged BrrG was used for ChIP-seq, then a WT non-tagged version should be used as a negative control (not sequencing INPUT DNA), this is especially important for anti-terminator that can co-travel with RNA polymerase. Please also report the number of replicates for ChIP-seq experiments.
Fig. 2A presents the coverage plot from the ChIP-Seq of ∆brrG +pPtet:3xFLAG-brrG (N’ in green). As anticipated by the referee, we had used ∆brrG +pTet:brrG (untagged) as control (grey). Each strain was tested in a single replicate. The C-terminal tag produced results similar to the untagged version, suggesting it is non-functional. All tested tags are shown in Supplementary Figure 2.
(4) Korotaev et al mentioned that BrrG binds to DNA (as well as to RNA polymerase). With the availability of existing ChIP-seq data, the authors should be able to locate the DNA-binding element of BrrG, this additional information will be useful to the community.
We identified a putative binding site of BrrG using our ChIP-Seq data. The putative binding site is indicated in Fig. 2D of the revised manuscript.
(5) Mutational experiments to break the potential hairpin structure are required to strengthen the claim that this putative hairpin is the potential transcriptional terminator.
We did not claim the identified hairpin is a confirmed terminator, but proposed it as a candidate. We agree with the referee that the suggested experiment would be necessary to definitively establish its function. However, our main objective was to show that BrrG acts as a processive terminator, which we demonstrated by replacing the putative terminator with a well-characterized synthetic one that BrrG successfully bypassed. Therefore, we chose not to perform the proposed experiment and have accordingly softened our conclusions regarding the hairpin’s potential terminator function.
Reviewer 2 (Public review):
Summary:
In this study, the authors identified and characterized a regulatory mechanism based on transcriptional anti-termination that connects the two gene clusters, capsid and run-off replication (ROR) locus, of the bipartite Bartonella gene transfer agent (GTA). Among genes essential for GTA functionality identified in a previous transposon sequencing project, they found a potential antiterminatior of phage origin within the ROR locus. They employed fluorescence reporter and gene transfer assays of overexpression and knockout strains in combination with ChiPSeq and promoter-fusions to convincingly show that this protein indeed acts as an antiterminator counteracting attenuation of the capsid gene cluster expression.
Impact on the field:
The results provide valuable insights into the evolution of the chimeric BaGTA, a unique example of phage co-domestication by bacteria. A similar system found in the other broadly studied Rhodobacterales/Caulobacterales GTA family suggests that antitermination could be a general mechanism for GTA control.
Strengths:
Results of the selected and carefully designed experiments support the main conclusions.
Weaknesses:
It remains open why overexpression of the antiterminator does not increase the gene transfer frequency.
We are grateful for reviewer #2's thoughtful and encouraging feedback on our manuscript. The reviewer raises an important question about why overexpression of the antiterminator does not increase gene transfer frequency. While we acknowledge this point, we consider it beyond the scope of the current study. Our findings clearly demonstrate that the antiterminator induces capsid component expression in a large proportion of cells. However, the fact that this expression plateaus at high levels rather than exhibiting a transient peak, as seen in the wild type, suggests that antiterminators do not regulate GTA particle release via lysis. We are actively investigating this further through additional experiments, which we plan to publish separately from this study.
Reviewer 2 (Recommendations for the authors):
(1) The authors wrote "GTAs are not self-transmitting because the DNA packaging capacity of a GTA particle is too small to package the entire gene cluster encoding it" (page 3). I thought that at least the Bartonella capsid gene cluster should be self-transmissible within the 14 kb packaged DNA (https://doi.org/10.1371/journal.pgen.1003393, https://doi.org/10.1371/journal.pgen.1000546). This was also concluded by Lang et al (https://doi.org/10.1146/annurev-virology-101416-041624). In this case the presented results would have important implications. As the gene cluster and the anti-terminator required for its expression are separated on the chromosome, it would not be possible to transfer an active GTA gene cluster, although the DNA coding for the genes required for making the packaging agent itself, theoretically fits into a BaGTA particle. Could the authors comment on that? I think it would be helpful to add the sizes of the different gene clusters and the distance between them in Fig. 2A. The ROR amplified region spans 500kb, is the capsid gene cluster within this region?
We thank the reviewer for bringing up this interesting point. The ror gene cluster, which encodes the antiterminator BrrG, is approximately 9.2 kb in size and could feasibly be packaged in its entirety into a GTA particle. In contrast, the bgt cluster (capsid cluster) is approximately 20 kb in size —exceeding the packaging limit of GTA particles—and is separated from the bgt cluster by approximately 35 kb. Consequently, if the ror cluster is transferred via a GTA particle into a recipient host that does not encode the bgt gene cluster, the ror cluster would not be expressed.
We added the sizes of the gene clusters to Fig. 1A.
(2) Another side-note regarding the introduction: On page three the authors write: "GTAs encode bacteriophage-like particles and in contrast to phages transfer random pieces of host bacterial DNA". While packaging is not specific, certain biases in the packaging frequency are observed in both studied GTA families. For Bartonella this is ROR. In the two GTA-producing strains D. shibae and C. crescentus origin and terminus of replication are not packaged and certain regions are overrepresented (https://doi.org/10.1093/gbe/evy005, https://doi.org/10.1371/journal.pbio.3001790). Furthermore, D. shibae plasmids are not packaged but chromids are. I think the term "random" does not properly describe these observations. I would suggest using "not specific" instead.
We thank the reviewer for this suggestion and adjusted the wording on p. 3 accordingly.
(3) Page 5: Remove "To address this". It is not needed as you already state "To test this hypothesis" in the previous sentence.
We adjusted the working on p.5 accordingly.
(4) I think the manuscript would greatly benefit from a summary figure to visualize the Q-like antiterminator-dependent regulatory circuit for GTA control and its four components described on pages 15 and 16.
We thank the reviewer for this valuable suggestion. We included a summary figure (Fig. 6) in the discussion section of the revised manuscript.
(5) Page 17: It might be worth noting that GafA is highly conserved along GTAs in Rhodobacterales (https://doi.org/10.3389/fmicb.2021.662907) and so is probably regulatory integration into the ctrA network (https://doi.org/10.3389/fmicb.2019.00803). It's an old mechanism. It would be also interesting to know if it is a common feature of the two archetypical GTAs that the regulator is not part of the cluster itself.
We agree with the reviewer’s comments and have revised the wording to state that GafA is highly conserved.
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Author response:
The following is the authors’ response to the original reviews
Public Reviews:
Reviewer #1 (Public Review):
In this study, the authors aim to understand why decision formation during behavioural tasks is distributed across multiple brain areas. They hypothesize that multiple areas are used in order to implement an information bottleneck (IB). Using neural activity recorded from monkey DLPFC and PMd performing a 2-AFC task, they show that DLPFC represents various task variables (decision, color, target configuration), while downstream PMd primarily represents decision information. Since decision information is the only information needed to make a decision, the authors point out that PMd has a minimal sufficient representation (as expected from an IB). They then train 3-area RNNs on the same task and show that activity in the first and third areas resemble the neural representations of DLPFC and PMd, respectively. In order to propose a mechanism, they analyse the RNN and find that area 3 ends up with primarily decision information because feedforward connections between areas primarily propagate decision information.
The paper addresses a deep, normative question, namely why task information is distributed across several areas.
Overall, it reads well and the analysis is well done and mostly correct (see below for some comments). My major problem with the paper is that I do not see that it actually provides an answer to the question posed (why is information distributed across areas?). I find that the core problem is that the information bottleneck method, which is evoked throughout the paper, is simply a generic compression method.
Being a generic compressor, the IB does not make any statements about how a particular compression should be distributed across brain areas - see major points (1) and (2).
If I ignore the reference to the information bottleneck and the question of why pieces of information are distributed, I still see a more mechanistic study that proposes a neural mechanism of how decisions are formed, in the tradition of RNN-modelling of neural activity as in Mante et al 2013. Seen through this more limited sense, the present study succeeds at pointing out a good model-data match, and I could support a publication along those lines. I point out some suggestions for improvement below.
We thank the reviewer for their comments, feedback and suggestions. We are glad to hear you support the good model-data match for this manuscript. With your helpful comments, we have clarified the connections to the information bottleneck principle and also contrasted it against the information maximization principle (the InfoMax principle), an alternative hypothesis. We elaborate on these issues in response to your points below, particularly major points (1) and (2). We also address all your other comments below.
Major points
(1) It seems to me that the author's use of the IB is based on the reasoning that deep neural networks form decisions by passing task information through a series of transformations/layers/areas and that these deep nets have been shown to implement an IB. Furthermore, these transformations are also loosely motivated by the data processing inequality.
On Major Point 1 and these following subpoints, we first want to make a high-level statement before delving into a detailed response to your points as it relates to the information bottleneck (IB). We hope this high-level statement will provide helpful context for the rest of our point-by-point responses.
We want to be clear that we draw on the information bottleneck (IB) principle as a general principle to explain why cortical representations differ by brain area. The IB principle, as applied to cortex, is only stating that a minimal sufficient representation to perform the task is formed in cortex, not how it is formed. The alternative hypothesis to the IB is that brain areas do not form minimal sufficient representations. For example, the InfoMax principle states that each brain area stores information about all inputs (even if they’re not necessary to perform the task). InfoMax isn’t unreasonable: it’s possible that storing as much information about the inputs, even in downstream areas, can support flexible computation and InfoMax also supports redundancy in cortical areas. Indeed, many studies claim that action choice related signals are in many cortical areas, which may reflect evidence of an InfoMax principle in action for areas upstream of PMd.
While we observe an IB in deep neural networks and cortex in our perceptual decision-making task, we stress that its emergence across multiple areas is an empirical result. At the same time, multiple areas producing an IB makes intuitive sense: due to the data processing inequality, successive transformations typically decrease the information in a representation (especially when, e.g., in neural networks, every activation passes through the Relu function, which is not bijective). Multiple areas are therefore a sufficient and even ‘natural’ way to implement an IB, but multiple areas are not necessary for an IB. That we observe an IB in deep neural networks and cortex emerge through multi-area computation is empirical, and, contrasting InfoMax, we believe it is an important result of this paper.
Nevertheless, your incisive comments have helped us to update the manuscript that when we talk about the IB, we should be clear that the alternative hypothesis is non-minimal representations, a prominent example of which is the InfoMax principle. We have now significantly revised our introduction to avoid this confusion. We hope this provides helpful context for our point-by-point replies, below.
However, assuming as a given that deep neural networks implement an IB does not mean that an IB can only be implemented through a deep neural network. In fact, IBs could be performed with a single transformation just as well. More formally, a task associates stimuli (X) with required responses (Y), and the IB principle states that X should be mapped to a representation Z, such that I(X;Z) is minimal and I(Y,Z) is maximal. Importantly, the form of the map Z=f(X) is not constrained by the IB. In other words, the IB does not impose that there needs to be a series of transformations. I therefore do not see how the IB by itself makes any statement about the distribution of information across various brain areas.
We agree with you that an IB can be implemented in a single transformation. We wish to be clear that we do not intend to argue necessity: that multiple areas are the only way to form minimal sufficient representations. Rather, multiple areas are sufficient to induce minimal sufficient representations, and moreover, they are a natural and reasonably simple way to do so. By ‘natural,’ we mean that minimal sufficient representations empirically arise in systems with multiple areas (more than 2), including deep neural networks and the cortex at least for our task and simulations. For example, we did not see minimal sufficient representations in 1- or 2-area RNNs, but we did see them emerge in RNNs with 3 areas or more. One potential reason for this result is that sequential transformations through multiple areas can never increase information about the input; it can only maintain or reduce information due to the data processing inequality.
Our finding that multiple areas facilitate IBs in the brain is therefore an empirical result: like in deep neural networks, we observe the brain has minimal sufficient representations that emerge in output areas (PMd), even as an area upstream (DLPFC) is not minimal. While the IB makes a statement that this minimal sufficient representation emerges, to your point, the fact that it emerges over multiple areas is not a part of the IB – as you have pointed out, the IB doesn’t state where or how the information is discarded, only that it is discarded. Our RNN modeling later proposes one potential mechanism for how it is discarded. We updated the manuscript introduction to make these points:
“An empirical observation from Machine Learning is that deep neural networks tend to form minimal sufficient representations in the last layers. Although multi-layer computation is not necessary for an IB, they provide a sufficient and even “natural” way to form an IB. A representation z = f(x) cannot contain more information than the input x itself due to the data processing inequality[19]. Thus, adding additional layers typically results in representations that contain less information about the input.”
And later in the introduction:
“Consistent with these predictions of the IB principle, we found that DLPFC has information about the color, target configuration, and direction. In contrast, PMd had a minimal sufficient representation of the direction choice. Our recordings therefore identified a cortical IB. However, we emphasize the IB does not tell us where or how the minimal sufficient representation is formed. Instead, only our empirical results implicate DLPFC-PMd in an IB computation. Further, to propose a mechanism for how this IB is formed, we trained a multi-area RNN to perform this task. We found that the RNN faithfully reproduced DLPFC and PMd activity, enabling us to propose a mechanism for how cortex uses multiple areas to compute a minimal sufficient representation.”
In the context of our work, we want to be clear the IB makes these predictions:
Prediction 1: There exists a downstream area of cortex that has a minimal and sufficient representation to perform a task (i.e.,. I(X;Z) is minimal while preserving task information so that I(Z;Y) is approximately equal to I(X;Y)). We identify PMd as an area with a minimal sufficient representation in our perceptual-decision-making task.
Prediction 2 (corollary if Prediction 1 is true): There exists an upstream brain area that contains more input information than the minimal sufficient area. We identify DLPFC as an upstream area relative to PMd, which indeed has more input information than downstream PMd in our perceptual decision-making task.
Note: as you raise in other points, it could have been possible that the IB is implemented early on, e.g., in either the parietal cortex (dorsal stream) or inferotemporal cortex (ventral stream), so that DLPFC and PMd both contained minimal sufficient representations. The fact that it doesn’t is entirely an empirical result from our data. If DLPFC had minimal sufficient representations for the perceptual decision making task, we would have needed to record in other regions to identify brain areas that are consistent with Prediction 2. But, empirically, we found that DLPFC has more input information relative to PMd, and therefore the DLPFC-PMd connection is implicated in the IB process.
What is the alternative hypothesis to the IB? We want to emphasize: it isn’t single-area computation. It’s that the cortex does not form minimal sufficient representations. For example, an alternative hypothesis (“InfoMax”) would be for all engaged brain areas to form representations that retain all input information. One reason this could be beneficial is because each brain area could support a variety of downstream tasks. In this scenario, PMd would not be minimal, invalidating Prediction 1. However, this is not supported by our empirical observations of the representations in PMd, which has a minimal sufficient representation of the task. We updated our introduction to make this clear:
“But cortex may not necessarily implement an IB. The alternative hypothesis to IB is that the cortex does not form minimal sufficient representations. One manifestation of this alternative hypothesis is the “InfoMax” principle, where downstream representations are not minimal but rather contain maximal input information22. This means information about task inputs not required to perform the task are present in downstream output areas. Two potential benefits of an InfoMax principle are (1) to increase redundancy in cortical areas and thereby provide fault tolerance, and (2) for each area to support a wide variety of tasks and thereby improve the ability of brain areas to guide many different behaviors. In contrast to InfoMax, the IB principle makes two testable predictions about cortical representations. Prediction 1: there exists a downstream area of cortex that has a minimal and sufficient representation to perform a task (i.e., I(X; Z) is minimal while preserving task information so that I(Z; Y) ≈ I(X; Y)). Prediction 2 (corollary if Prediction 1 is true): there exists an upstream area of cortex that has more task information than the minimal sufficient area.”
Your review helped us realize we should have been clearer in explaining that these are the key predictions of the IB principle tested in our paper. We also realized we should be much clearer that these predictions aren’t trivial or expected, and there is an alternative hypothesis. We have re-written the introduction of our paper to highlight that the key prediction of the IB is minimal sufficient representations for the task, in contrast to the alternative hypothesis of InfoMax.
A related problem is that the authors really only evoke the IB to explain the representation in PMd: Fig 2 shows that PMd is almost only showing decision information, and thus one can call this a minimal sufficient representation of the decision (although ignoring substantial condition independent activity).
However, there is no IB prediction about what the representation of DLPFC should look like.
Consequently, there is no IB prediction about how information should be distributed across DLPFC and PMd.
We agree: the IB doesn’t tell us how information is distributed, only that there is a transformation that eventually makes PMd minimal. The fact that we find input information in DLPFC reflects that this computation occurs across areas, and is an empirical characterization of this IB in that DLPFC has direction, color and context information while PMd has primarily direction information. To be clear: only our empirical recordings verified that the DLPFC-PMd circuit is involved in the IB. As described above, if not, we would have recorded even further upstream to identify an inter-areal connection implicated in the IB.
We updated the text to clearly state that the IB predicts that an upstream area’s activity should contain more information about the task inputs. We now explicitly describe this in the introduction, copy and pasted again here for convenience.
“In contrast to InfoMax, the IB principle makes two testable predictions about cortical representations. Prediction 1: there exists a downstream area of cortex that has a minimal and sufficient representation to perform a task (i.e., I(X; Z) is minimal while preserving task information so that I(Z; Y) ≈ I(X; Y)). Prediction 2 (corollary if Prediction 1 is true): there exists an upstream area of cortex that has more task information than the minimal sufficient area.
Consistent with the predictions of the IB principle, we found that DLPFC has information about the color, target configuration, and direction. In contrast, PMd had a minimal sufficient representation of the direction choice. Our recordings therefore identified a cortical IB. However, we emphasize the IB does not tell us where or how the minimal sufficient representation is formed. Instead, only our empirical results implicate DLPFC-PMd in an IB computation Further, to propose a mechanism for how this IB is formed, we trained a multi-area RNN to perform this task.”
The only way we knew DLPFC was not minimal was through our experiments. Please also note that the IB principle does not describe how information could be lost between areas or layers, whereas our RNN simulations show that this may occur through preferential propagation of task-relevant information with respect to the inter-area connections.
(2) Now the authors could change their argument and state that what is really needed is an IB with the additional assumption that transformations go through a feedforward network. However, even in this case, I am not sure I understand the need for distributing information in this task. In fact, in both the data and the network model, there is a nice linear readout of the decision information in dPFC (data) or area 1 (network model). Accordingly, the decision readout could occur at this stage already, and there is absolutely no need to tag on another area (PMd, area 2+3).
Similarly, I noticed that the authors consider 2,3, and 4-area models, but they do not consider a 1-area model. It is not clear why the 1-area model is not considered. Given that e.g. Mante et al, 2013, manage to fit a 1-area model to a task of similar complexity, I would a priori assume that a 1-area RNN would do just as well in solving this task.
While decision information could indeed be read out in Area 1 in our multi-area model, we were interested in understanding how the network converged to a PMd-like representation (minimal sufficient) for solving this task. Empirically, we only observed a match between our model representations and animal cortical representations during this task when considering multiple areas. Given that we empirically observed that our downstream area had a minimal sufficient representation, our multi-area model allowed how this minimal sufficient representation emerged (through preferential propagation of task-relevant information).
We also analyzed single-area networks in our initial manuscript, though we could have highlighted these analyses more clearly to be sure they were not overlooked. We are clearer in this revision that we did consider a 1-area network (results in our Fig 5). While a single-area RNN can indeed solve this task, the single area model had all task information present in the representation, and did not match the representations in DLPFC or PMd. It would therefore not allow us to understand how the network converged to a PMd-like representation (minimal sufficient) for solving this task. We updated the schematic in Fig 5 to add in the single-area network (which may have caused the confusion).
We have added an additional paragraph commenting on this in the discussion. We also added an additional supplementary figure with the PCs of the single area RNN (Fig S15). We highlight that single area RNNs do not resemble PMd activity because they contain strong color and context information.
In the discussion:
“We also found it was possible to solve this task with single area RNNs, although they did not resemble PMd (Figure S15) since it did not form a minimal sufficient representation. Rather, for our RNN simulations, we found that the following components were sufficient to induce minimal sufficient representations: (1) RNNs with at least 3 areas, following Dale’s law (independent of the ratio of feedforward to feedback connections).”
I think there are two more general problems with the author's approach. First, transformations or hierarchical representations are usually evoked to get information into the right format in a pure feedforward network. An RNN can be seen as an infinitely deep feedforward network, so even a single RNN has, at least in theory, and in contrast to feedforward layers, the power to do arbitrarily complex transformations. Second, the information coming into the network here (color + target) is a classical xor-task. While this task cannot be solved by a perceptron (=single neuron), it also is not that complex either, at least compared to, e.g., the task of distinguishing cats from dogs based on an incoming image in pixel format.
An RNN can be viewed as an infinitely deep feedforward network in time. However, we wish to clarify two things. First, our task runs for a fixed amount of time, and therefore this RNN in practice is not infinitely deep in time. Second, if it were to perform an IB operation in time, we would expect to see color discriminability decrease as a function of time. Indeed, we considered this as a mechanism (recurrent attenuation, Figure 4a), but as we show in Supplementary Figure S9, we do not observe it to be the case that discriminability decreases through time. This is equivalent to a dynamical mechanism that removes color through successive transformations in time, which our analyses reject (Fig 4). We therefore rule out that an IB is implemented through time via an RNN’s recurrent computation (viewed as feedforward in time). Rather, as we show, the IB comes primarily through inter-areal connections between RNN areas. We clarified that our dynamical hypothesis is equivalent to rejecting the feedforward-in-time filtering hypothesis in the Results:
“We first tested the hypothesis that the RNN IB is implemented primarily by recurrent dynamics (left side of Fig. 4a). These recurrent dynamics can be equivalently interpreted as the RNN implementing a feedforward neural network in time.”
The reviewer is correct that the task is a classical XOR task and not as complex as e.g., computer vision classification. That said, our related work has looked at IBs for computer vision tasks and found them in deep feedforward networks (Kleinman et al., ICLR 2021). Even though the task is relatively straightforward, we believe it is appropriate for our conclusions because it does not have a trivial minimal sufficient representation: a minimal sufficient representation for XOR must contain only target, but not color or target configuration information. This can only be solved via a nonlinear computation. In this manner, we favor this task because it is relatively simple, and the minimal sufficient representations are interpretable, while at the same time not being so trivially simple (the minimal sufficient representations require nonlinearity to compute).
Finally, we want to note that this decision-making task is a logical and straightforward way to add complexity to classical animal decision-making tasks, where stimulus evidence and the behavioral report are frequently correlated. In tasks such as these, it may be challenging to untangle stimulus and behavioral variables, making it impossible to determine if an area like premotor cortex represents only behavior rather than stimulus. However, our task decorrelates both the stimulus and the behaviors.
(3) I am convinced of the author's argument that the RNN reproduces key features of the neural data. However, there are some points where the analysis should be improved.
(a) It seems that dPCA was applied without regularization. Since dPCA can overfit the data, proper regularization is important, so that one can judge, e.g., whether the components of Fig.2g,h are significant, or whether the differences between DLPFC and PMd are significant.
We note that the dPCA codebase optimizes the regularization hyperparameter through cross-validation and requires single-trial firing rates for all neurons, i.e., data matrices of the form (n_Neurons x Color x Choice x Time x n_Trials), which are unavailable for our data. We recognized that you are fundamentally asking whether differences are significant or not. We therefore believe it is possible to address this through a statistical test, described further below.
In order to test whether the differences of variance explained by task variables between DLPFC and PMd are significant, we performed a shuffle test. For this test, we randomly sampled 500 units from the DLPFC dataset and 500 units from the PMd dataset. We then used dPCA to measure the variance explained by target configuration, color choice, and reach direction (e.g., Var<sup>True</sup><sub>DLPFC,Color</sub>, Var<sup>True</sup><sub>PMd,Color</sub>).
To test if this variance was significant, we performed the following shuffle test. We combined the PMd and DLPFC dataset into a pool of 1000 units and then randomly selected 500 units from this pool to create a surrogate PMd dataset and used the remaining 500 units as a surrogate DLPFC dataset. We then again performed dPCA on these surrogate datasets and estimated the variance for the various task variables (e.g., Var<sub>ShuffledDLPFC,Color</sub> ,Var<sub>ShuffledPMd,Color</sub>).
We repeated this process for 100 times and estimated a sampling distribution for the true difference in variance between DLPFC and PMd for various task variables (e.g., Var<sup>True</sup><sub>DLPFC,Color</sub> - Var<sup>True</sup><sub>PMd,Color</sub>). At the same time, we estimated the distribution of the variance difference between surrogate PMd and DLPFC dataset for various task variables (e.g., Var<sub>ShuffleDLPFC,Color</sub> - Var<sub>ShufflePMd,Color</sub>).
We defined a p-value as the number of shuffles in which the difference in variance was higher than the median of the true difference and divided it by 100. Note, for resampling and shuffle tests with n shuffles/bootstraps, the lowest theoretical p-value is given as 2/n, even in the case that no shuffle was higher than the median of the true distribution. Thus, the differences were statistically significant (p < 0.02) for color and target configuration but not for direction (p=0.72). These results are reported in Figure S6 and show both the true sampling distribution and the shuffled sampling distributions.
(b) I would have assumed that the analyses performed on the neural data were identical to the ones performed on the RNN data. However, it looked to me like that was not the case. For instance, dPCA of the neural data is done by restretching randomly timed trials to a median trial. It seemed that this restretching was not performed on the RNN. Maybe that is just an oversight, but it should be clarified. Moreover, the decoding analyses used SVC for the neural data, but a neural-net-based approach for the RNN data. Why the differences?
Thanks for bringing up these points. We want to clarify that we did include SVM decoding for the multi-area network in the appendix (Fig. S4), and the conclusions are the same. Moreover, in previous work, we also found that training with a linear decoder led to analogous conclusions (Fig. 11 of Kleinman et al, NeurIPS 2021). As we had a larger amount of trials for the RNN than the monkey, we wanted to allow a more expressive decoder for the RNN, though this choice does not affect our conclusions. We clarified the text to reflect that we did use an SVM decoder.
“We also found analogous conclusions when using an SVM decoder (Fig. S4).”
dPCA analysis requires trials of equal length. For the RNN, this is straightforward to generate because we can set the delay lengths to be equal during inference (although the RNN was trained on various length trials and can perform various length trials). Animals must have varying delay periods, or else they will learn the timing of the task and anticipate epoch changes. Because animal trial lengths were therefore different, their trials had to be restretched. We clarified this in the Methods.
“For analyses of the RNN, we fixed the timing of trials, obviating the need to to restretch trial lengths. Note that while at inference, we generated RNN trials with equal length, the RNN was trained with varying delay periods.”
(4) The RNN seems to fit the data quite nicely, so that is interesting. At the same time, the fit seems somewhat serendipitous, or at least, I did not get a good sense of what was needed to make the RNN fit the data. The authors did go to great lengths to fit various network models and turn several knobs on the fit. However, at least to me, there are a few (obvious) knobs that were not tested.
First, as already mentioned above, why not try to fit a single-area model? I would expect that a single area model could also learn the task - after all, that is what Mante et al did in their 2013 paper and the author's task does not seem any more complex than the task by Mante and colleagues.
Thank you for bringing up this point. As mentioned in response to your prior point, we did analyze a single-area RNN (Fig. 5d). We updated the schematic to clarify that we analyzed a single area network. Moreover, we also added a supplementary figure to qualitatively visualize the PCs of the single area network (Fig. S15). While a single area network can solve the task, it does not allow us to study how representations change across areas, nor did it empirically resemble our neural recordings. Single-area networks contain significant color, context, and direction information. They therefore do not form minimal representations and do not resemble PMd activity.
Second, I noticed that the networks fitted are always feedforward-dominated. What happens when feedforward and feedback connections are on an equal footing? Do we still find that only the decision information propagates to the next area? Quite generally, when it comes to attenuating information that is fed into the network (e.g. color), then that is much easier done through feedforward connections (where it can be done in a single pass, through proper alignment or misalignment of the feedforward synapses) than through recurrent connections (where you need to actively cancel the incoming information). So it seems to me that the reason the attenuation occurs in the inter-area connections could simply be because the odds are a priori stacked against recurrent connections. In the real brain, of course, there is no clear evidence that feedforward connections dominate over feedback connections anatomically.
We want to clarify that we did pick feedforward and feedback connections based on the following macaque atlas, reference 27 in our manuscript:
Markov, N. T., Ercsey-Ravasz, M. M., Ribeiro Gomes, A. R., Lamy, C., Magrou, L., Vezoli, J., Misery, P., Falchier, A., Quilodran, R., Gariel, M. A., Sallet, J., Gamanut, R., Huissoud, C., Clavagnier, S., Giroud, P., Sappey-Marinier, D., Barone, P., Dehay, C., Toroczkai, Z., … Kennedy, H. (2014). A weighted and directed interareal connectivity matrix for macaque cerebral cortex. Cerebral Cortex , 24(1), 17–36.
We therefore believe there is evidence for more feedforward than feedback connections. Nevertheless, as stated in response to your next point below, we ran a simulation where feedback and feedforward connectivity were matched.
More generally, it would be useful to clarify what exactly is sufficient:
(a) the information distribution occurs in any RNN, i.e., also in one-area RNNs
(b) the information distribution occurs when there are several, sparsely connected areas
(c) the information distribution occurs when there are feedforward-dominated connections between areas
We better clarify what exactly is sufficient.
- We trained single-area RNNs and found that these RNNs contained color information; additionally two area RNNs also contained color information in the last area (Fig 5d).
- We indeed found that the minimal sufficient representations emerged when we had several areas, with Dale’s law constraint on the connectivity. When we had even sparser connections, without Dale’s law, there was significantly more color information, even at 1% feedforward connections; Fig 5a.
- When we matched the percentage of feedforward and feedback connections with Dale’s law constraint on the connectivity (10% feedforward and 10% feedback), we also observed minimal sufficient representations (Fig S9).
Together, we found that minimal sufficient representations emerged when we had several areas (3 or greater), with Dale’s law constraint on the connectivity, independent of the ratio of feedforward/feedback connections. We thank the reviewer for raising this point about the space of constraints leading to minimal sufficient representations in the late area. We clarified this in the Discussion.
“We also found it was possible to solve this task with single area RNNs, although they did not resemble PMd (Figure S15) since it did not form a minimal sufficient representation. Rather, for our RNN simulations, we found that the following components were sufficient to induce minimal sufficient representations: RNNs with at least 3 areas, following Dale’s law (independent of the ratio of feedforward to feedback connections).”
Thank you for your helpful and constructive comments!
Reviewer #2 (Public Review):
Kleinman and colleagues conducted an analysis of two datasets, one recorded from DLPFC in one monkey and the other from PMD in two monkeys. They also performed similar analyses on trained RNNs with various architectures.
The study revealed four main findings. (1) All task variables (color coherence, target configuration, and choice direction) were found to be encoded in DLPFC. (2) PMD, an area downstream of PFC, only encoded choice direction. (3) These empirical findings align with the celebrated 'information bottleneck principle,' which suggests that FF networks progressively filter out task-irrelevant information. (4) Moreover, similar results were observed in RNNs with three modules.
We thank the reviewer for their comments, feedback and suggestions, which we address below.
While the analyses supporting results 1 and 2 were convincing and robust, I have some concerns and recommendations regarding findings 3 and 4, which I will elaborate on below. It is important to note that findings 2 and 4 had already been reported in a previous publication by the same authors (ref. 43).
Note the NeurIPS paper only had PMd data and did not contain any DLPFC data. That manuscript made predictions about representations and dynamics upstream of PMd, and subsequent experiments reported in this manuscript validated these predictions. Importantly, this manuscript observes an information bottleneck between DLPFC and PMd.
Major recommendation/comments:
The interpretation of the empirical findings regarding the communication subspace in relation to the information bottleneck theory is very interesting and novel. However, it may be a stretch to apply this interpretation directly to PFC-PMd, as was done with early vs. late areas of a FF neural network.
In the RNN simulations, the main finding indicates that a network with three or more modules lacks information about the stimulus in the third or subsequent modules. The authors draw a direct analogy between monkey PFC and PMd and Modules 1 and 3 of the RNNs, respectively. However, considering the model's architecture, it seems more appropriate to map Area 1 to regions upstream of PFC, such as the visual cortex, since Area 1 receives visual stimuli. Moreover, both PFC and PMd are deep within the brain hierarchy, suggesting a more natural mapping to later areas. This contradicts the CCA analysis in Figure 3e. It is recommended to either remap the areas or provide further support for the current mapping choice.
We updated the Introduction to better clarify the predictions of the information bottleneck (IB) principle. In particular, the IB principle predicts that later areas should have minimal sufficient representations of task information, whereas upstream areas should have more information. In PMd, we observed a minimal sufficient representation of task information during the decision-making task. In DLPFC, we observed more task information, particularly more information about the target colors and the target configuration.
In terms of the exact map between areas, we do not believe or intend to claim the DLPFC is the first area implicated in the sensorimotor transformation during our perceptual decision-making task. Rather, DLPFC best matches Area 1 of our model. It is important to note that we abstracted our task so that the first area of our model received checkerboard coherence and target configuration as input (and hence did not need to transform task visual inputs). Indeed, in Figure 1d we hypothesize that the early visual areas should contain additional information, which we do not model directly in this work. Future work could model RNNs to take in an image or video input of the task stimulus. In this case, it would be interesting to assess if earlier areas resemble visual cortical areas. We updated the results, where we first present the RNN, to state the inputs explicitly and be clear the inputs are not images or videos of the checkerboard task.
“The RNN input was 4D representing the target configuration and checkerboard signed coherence, while the RNN output was 2D, representing decision variables for a left and right reach (see Methods).”
Another reason that we mapped Area 1 to DLPFC is because anatomical, physiological and lesion studies suggest that DLPFC receives inputs from both the dorsal and ventral stream (Romanski, et, al, 2007; Hoshi, et al, 2006; Wilson, at al, 1993). The dorsal stream originates from the occipital lobe, passes through the posterior parietal cortex, to DLPFC, which carries visuospatial information of the object. The ventral stream originates from the occipital lobe, passes through the inferior temporal cortex, ventrolateral prefrontal cortex to DLPFC, which encodes the identity of the object, including color and texture. In our RNN simulation, Area 1 receives processed inputs of the task: target configuration and the evidence for each color in the checkerboard. Target configuration contains information of the spatial location of the targets, which represents the inputs from the dorsal stream, while evidence for each color by analogy is the input from the ventral stream. Purely visual areas would not fit this dual input from both the dorsal and ventral stream. A potential alternative candidate would be the parietal cortex which is largely part of the dorsal stream and is thought to have modest color inputs (although there is some shape and color selectivity in areas such as LIP, e.g., work from Sereno et al.). On balance given the strong inputs from both the dorsal and ventral stream, we believe Area 1 maps better on to DLPFC than earlier visual areas.
Recommendations for the authors:
Reviewer #1 (Recommendations For The Authors):
(1) Line 35/36: Please specify the type of nuisance that the representation is robust to. I guess this refers to small changes in the inputs, not to changes in the representation itself.
Indeed it refers to input variability unrelated to the task. We clarified the text.
(2) For reference, it would be nice to have a tick for the event "Targets on" in Fig.2c.
In this plot, the PSTHs are aligned to the checkerboard onset. Because there is a variable time between target and checkerboard onset, there is a trial-by-trial difference of when the target was turned on, so there is no single place on the x-axis where we could place a “Targets on” tick. In response to this point, we generated a plot with both targets on and check on alignment, with a break in the middle, shown in Supplementary Figure S5.
(3) It would strengthen the comparison between neural data and RNN if the DPCA components of the RNN areas were shown, as they are shown in Fig.2g,h for the neural data.
We include the PSTHs plotted onto the dPCA components here for Area 1 of the exemplar network. Dashed lines indicate a left reach, while solid lines indicate a right reach, and the color corresponds to the color of the selected target. As expected, we find that the dPCA components capture the separation between components. We emphasize that the trajectory paths along the decoder axes are not particularly meaningful to interpret, except to demonstrate whether variables can be decoded or not (as in Fig 2g,h, comparing DLPFC and PMd). The decoder axes of dPCA are not constrained in any way, in contrast to the readout (encoder) axis (see Methods). This is why our manuscript focuses on analyzing the readout axes. However, if the reviewer strongly prefers these plots to be put in the manuscript, we will add them.
Author response image 1.
(4) The session-by-session decode analysis presented in Fig.2i suggests that DLPFC has mostly direction information while in Area 1 target information is on top, as suggested by Fig.3g. An additional decoding analysis on trial averaged neural data, i.e. a figure for neural data analogous to Fig.3g,h, would allow for a more straightforward and direct comparison between RNN and neural data.
We first clarify that we did not decode trial-averaged neural data for either recorded neural data or RNNs. In Fig 3g, h (for the RNN) all decoding was performed on single trial data and then averaged. We have revised the main manuscript to make this clear. Because of this, the mean accuracies we reported for DLPFC and PMd in the text are therefore computed in the same way as the mean accuracies presented in Fig 3g, h. We believe this likely addresses your concern: i.e., the mean decode accuracies presented for both neural data and the RNN were computed the same way.
If the above paragraph did not address your concern, we also wish to be clear that we presented the neural data as histograms, rather than a mean with standard error, because we found that accuracies were highly variable depending on electrode insertion location. For example, some insertions in DLPFC achieved chance-levels of decoding performance for color and target configuration. For this reason, we prefer to keep the histogram as it shows more information than reporting the mean, which we report in the main text. However, if the reviewer strongly prefers us to make a bar plot of these means, we will add them.
(5) Line 129 mentions an analysis of single trials. But in Fig.2i,j sessions are analyzed. Please clarify.
For each session, we decode from single trials and then average these decoding accuracies, leading to a per-session average decoding accuracy. Note that for each session, we record from different neurons. In the text, we also report the average over the sessions. We clarified this in the text and Methods.
(6) Fig.4c,f show how color and direction axes align with the potent subspaces. We assume that the target axis was omitted here because it highly aligns with the color axis, yet we note that this was not pointed out explicitly.
You are correct, and we revised the text to point this out explicitly.
“We quantified how the color and direction axis were aligned with these potent and null spaces of the intra-areal recurrent dynamics matrix of Area 1 ($\W^1_{rec}$). We did not include the target configuration axis for simplicity, since it highly aligns with the color axis for this network.”
(7) The caption of Fig.4c reads: "Projections onto the potent space of the intra-areal dynamics for each area." Yet, they only show area 1 in Fig.4c, and the rest in a supplement figure. Please refer properly.
Thank you for pointing this out. We updated the text to reference the supplementary figure.
(8) Line 300: "We found the direction axis was more aligned with the potent space and the color axis was more aligned with the null space." They rather show that the color axis is as aligned to the potent space as a random vector, but nothing about the alignments with the null space. Contrarily, on line 379 they write "...with the important difference that color information isn't preferentially projected to a nullspace...". Please clarify.
Thank you for pointing this out. We clarified the text to read: “We found the direction axis was more aligned with the potent space”. The text then describes that the color axis is aligned like a random vector: “In contrast, the color axis was aligned to a random vector.”
(9) Line 313: 'unconstrained' networks are mentioned. What constraints are implied there, Dale's law? Please define and clarify.
Indeed, the constraint refers to Dale’s law constraints. We clarified the text: “Further, we found that W<sub>21</sub> in unconstrained 3 area networks (i.e., without Dale's law constraints) had significantly reduced…”
(10) Line 355 mentions a 'feedforward bottleneck'. What does this exactly mean? No E-I feedforward connections, or...? Please define and clarify.
This refers to sparser connections between areas than within an area, as well as a smaller fraction of E-I connections. We clarified the text to read:
“Together, these results suggest that a connection bottleneck in the form of neurophysiological architecture constraints (i.e., sparser connections between areas than within an area, as well as a smaller fraction of E-I connections) was the key design choice leading to RNNs with minimal color representations and consistent with the information bottleneck principle.”
(11) Fig.5c is supposedly without feedforward connections, but it looks like the plot depicts these connections (i.e. identical to Fig.5b).
In Figure 5, we are varying the E to I connectivity in panel B, and the E-E connectivity in panel C. We vary the feedback connections in Supp Fig. S12. We updated the caption accordingly.
(12) For reference, it would be nice to have the parameters of the exemplar network indicated in the panels of Fig.5.
We updated the caption to reference the parameter configuration in Table 1 of the Appendix.
(13) Line 659: incomplete sentence
Thank you for pointing this out. We removed this incomplete sentence.
(14) In the methods section "Decoding and Mutual information for RNNs" a linear neural net decoder as well as a nonlinear neural net decoder are described, yet it was unclear which one was used in the end.
We used the nonlinear network, and clarified the text accordingly. We obtained consistent conclusions using a linear network, but did not include these results in the text. (These are reported in Fig. 11 of Kleinman et al, 2021). Moreover, we also obtain consistent results by using an SVM decoder in Fig. S4 for our exemplar parameter configuration.
(15) In the discussion, the paragraph starting from line 410 introduces a new set of results along with the benefits of minimal representations. This should go to the results section.
We prefer to leave this as a discussion, since the task was potentially too simplistic to generate a clear conclusion on this matter. We believe this remains a discussion point for further investigation.
(16) Fig S5: hard to parse. Show some arrows for trajectories (a) (d) is pretty mysterious: where do I see the slow dynamics?
Slow points are denoted by crosses, which forms an approximate line attractor. We clarified this in the caption.
Reviewer #2 (Recommendations For The Authors):
Minor recommendations (not ordered by importance)
(1) Be more explicit that the recordings come from different monkeys and are not simultaneously recorded. For instance, say 'recordings from PFC or PMD'. Say early on that PMD recordings come from two monkeys and that PFC recordings come from 1 of those monkeys. Furthermore, I would highlight which datasets are novel and which are not. For instance, I believe the PFC dataset is a previously unpublished dataset and should be highlighted as such.
We added: “The PMd data was previously described in a study by Chandrasekaran and colleagues” to the main text which clarifies that the PMd data was previously recorded and has been analyzed in other studies.
(2) I personally feel that talking about 'optimal', as is done in the abstract, is a bit of a stretch for this simple task.
In using the terminology “optimal,” we are following the convention of IB literature that optimal representations are sufficient and minimal. The term “optimal” therefore is task-specific; every task will have its own optimal representation. We clarify in the text that this definition comes from Machine Learning and Information Theory, stating:
“The IB principle defines an optimal representation as a representation that is minimal and sufficient for a task or set of tasks.”
In this way, we take an information-theoretic view for describing multi-area representations. This view was satisfactory for explaining and reconciling the multi-area recordings and simulations for this task, and we think it is helpful to provide a normative perspective for explaining the differences in cortical representations by brain area. Even though the task is simple, it still allows us to study how sensory/perceptual information is represented, and well as how choice-related information is being represented.
(3) It is mentioned (and even highlighted) in the abstract that we don't know why the brain distributes computations. I agree with that statement, but I don't think this manuscript answers that question. Relatedly, the introduction mentions robustness as one reason why the brain would distribute computations, but then raises the question of whether there is 'also a computational benefit for distributing computations across multiple areas'. Isn't the latter (robustness) a clear 'computational benefit'?
We decided to keep the word “why” in the abstract, because this is a generally true statement (it is unclear why the brain distributes computation) that we wish to convey succinctly, pointing to the importance of studying this relatively grand question (which could only be fully answered by many studies over decades). We consider this the setting of our work. However, to avoid confusion that we are trying to give a full answer to this question, we are now more precise in the first paragraph of our introduction as to the particular questions we ask that will take a step towards this question. In particular, the first paragraph now asks these questions, which we answer in our study.
“For example, is all stimuli and decision-related information present in all brain areas, or do the cortical representations differ depending on their processing stage? If the representations differ, are there general principles that can explain why the cortical representations differ by brain area?”
We also removed the language on robustness, as we agree it was confusing. Thank you for these suggestions.
(4) Figure 2e and Fig. 3d, left, do not look very similar. I suggest zooming in or rotating Figure 2 to highlight the similarities. Consider generating a baseline CCA correlation using some sort of data shuffle to highlight the differences.
The main point of the trajectories is to demonstrate that both Area 1 and DLPFC represent both color and direction. We now clarify this in the manuscript. However, we do not intend for these two plots to be a rigorous comparison of similarity. Rather, we quantify similarity using CCA and our decoding analysis. We also better emphasize the relative values of the CCA, rather than the absolute values.
(5) Line 152: 'For this analysis, we restricted it to sessions with significant decode accuracy with a session considered to have a significant decodability for a variable if the true accuracy was above the 99th percentile of the shuffled accuracy for a session.' Why? Sounds fishy, especially if one is building a case on 'non-decodability'. I would either not do it or better justify it.
The reason to choose only sessions with significant decoding accuracy is that we consider those sessions to be the sessions containing information of task variables. In response to this comment, we also now generate a plot with all recording sessions in Supplementary Figure S7. We modified the manuscript accordingly.
“For this analysis, we restricted it to sessions with significant decode accuracy with a session considered to have a significant decodability for a variable if the true accuracy was above the 99th percentile of the shuffled accuracy for a session. This is because these sessions contain information about task variables. However, we also present the same analyses using all sessions in Fig. S7.”
(6) Line 232: 'The RNN therefore models many aspects of our physiological data and is therefore'. Many seems a stretch?
We changed “many” to “key.”
(7) The illustration in Fig. 4B is very hard to understand, I recommend removing it.
We are unsure what this refers to, as Figure 4B represents data of axis overlaps and is not an illustration.
(8) At some point the authors use IB instead of information bottleneck (eg line 288), I would not do it.
We now clearly write that IB is an abbreviation of Information Bottleneck the first time it is introduced.
(9) Fig. 5 caption is insufficient to understand it. Text in the main document does not help. I would move most part of this figure, or at least F, to supplementary. Instead, I would move the results in S11 and S10 to the main document.
We clarified the caption to summarize the key points. It now reads:
“Overall, neurophysiological architecture constraints in the form of multiple areas, sparser connections between areas than within an area, as well as a smaller fraction of E-I connections lead to a minimal color representation in the last area.”
(10) Line 355: 'Together, these results suggest that a connection bottleneck in the form of neurophysiological architecture constraints was the key design choice leading to RNNs with minimal color representations and consistent with the information bottleneck principle.' The authors show convincingly that increased sparsity leads to the removal of irrelevant information. There is an alternative model of the communication subspace hypothesis that uses low-rank matrices, instead of sparse, to implement said bottlenecks (https://www.biorxiv.org/content/10.1101/2022.07.21.500962v2)
We thank the reviewer for pointing us to this very nice paper. Indeed, a low-rank connectivity matrix is another mechanism to limit the amount of information that is passed to subsequent areas. In fact, the low-rank matrix forms a hard-version of our observations as we found that task-relevant information was preferentially propagated along the top singular mode of the inter-areal connectivity matrix. In our paper we observed this tendency naturally emerges through training with neurophysiological architecture constraints. In the paper, for the multi-area RNN, they hand-engineered the multi-area network, whereas our network is trained. We added this reference to our discussion.
Thank you for your helpful and constructive comments.
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CH and CN
This seems mostly due to the methylcellulose, correct? I'm wondering if there is a way to determine the actual number of anchor points in the liposome? Perhaps some staining against the His tag? It might be interesting to see where deformations lie in relation to clusters of anchor points.
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F-actin is 1.4 μM
Do you also have the Kd of untagged actinin for F-actin? It could be nice to know if the tag has any impact on binding. I'm also curious if the membrane tethered actinin has a different affinity for actin filaments compared to free-floating actinin.
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Universal Sync
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Faster Sync
Peergos Sync
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This image lacks a descriptive alt tag. According to the WCAG guidelines and our course, this makes the content inaccessible to users relying on screen readers, a violation of the Perceivable principle.
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fakepixels.substack.com fakepixels.substack.com
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Leisure's opportunity cost skyrockets. When an hour of work generates what once took days, rest becomes luxury taxed by your own conscience. Every pause carries an invisible price tag that flickers in your peripheral vision.Productivity breeds new demand. Like efficient engines creating new energy uses, AI can create entirely new work categories and expectations.Competition intensifies. The game theory is unforgiving: when everyone can produce 10x more, the baseline resets, leaving us all running faster just to stay in place.
Consequences
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Reviewer #3 (Public review):
Summary:
In this study, Kito et al follow up on previous work that identified Drosophila GCL as a mitotic substrate recognition subunit of a CUL3-RING ubiquitin ligase (CRL3) complex.
Here they characterize mutants of the human ortholog of GCL, GMCL1, that disrupt the interaction with CUL3 (GMCL1E142K) and that lack the substrate interaction domain (GMCL1 BBO). Immunoprecipitation followed by mass spectrometry identified 9 proteins that interacted with wild-type FLAG-GMCL1 and GMCL1 EK but not GMCL1 BBO. These proteins included 53BP1, which plays a well-characterized role in double-strand break repair but also functions in a USP28-p53-53BP1 "mitotic stopwatch" complex that arrests the cell cycle after a substantially prolonged mitosis. Consistent with the IP-MS results, FLAG-GMCL1 immunoprecipitated 53BP1. Depletion of GMCL1 during mitotic arrest increased protein levels of 53BP1, and this could be rescued by wild-type GMCL1 but not the E142K mutant or a R433A mutant that failed to immunoprecipitate 53BP1.
Using a publicly available dataset, the authors identified a relatively small subset of cell lines with high levels of GMCL1 mRNA that were resistant to the taxanes paclitaxel, cabazitaxel, and docetaxel. This type of analysis is confounded by the fact that paclitaxel and other microtubule poisons accumulate to substantially different levels in various cell lines (DOI: 10.1073/pnas.90.20.9552 , DOI: 10.1091/mbc.10.4.947 ), so careful follow-up experiments are required to validate results. The correlation between increased GMCL1 mRNA and taxane resistance was not observed in lung cancer cell lines. The authors propose this was because nearly half of lung cancers harbor p53 mutations, and lung cancer cell lines with wild-type but not mutant p53 showed the correlation between increased GMCL1 mRNA and taxane resistance. However, the other cancer cell types in which they report increased GMCL1 expression correlates with taxane sensitivity also have high rates of p53 mutation. Furthermore, p53 status does not predict taxane response in patients (DOI: 10.1002/1097-0142(20000815)89:4<769::aid-cncr8>3.0.co;2-6 , DOI: 10.1002/(SICI)1097-0142(19960915)78:6<1203::AID-CNCR6>3.0.CO;2-A , PMID: 10955790).
The authors then depleted GMCL1 and reported that it increased apoptosis in two cell lines with wild-type p53 (MCF7 and U2OS) due to activation of the mitotic stopwatch. This is surprising because the mitotic stopwatch paper they cite (DOI: 10.1126/science.add9528 ) reported that U2OS cells have an inactive stopwatch and that activation of the stopwatch results in cell cycle arrest rather than apoptosis in most cell types, including MCF7. Beyond this, it has recently been shown that the level of taxanes and other microtubule poisons achieved in patient tumors is too low to induce mitotic arrest (DOI: 10.1126/scitranslmed.3007965 , DOI: 10.1126/scitranslmed.abd4811 , DOI: 10.1371/journal.pbio.3002339 ), raising concerns about the relevance of prolonged mitosis to paclitaxel response in cancer. The findings here demonstrating that GMCL1 mediates degradation of 53BP1 during mitotic arrest are solid and of interest to cell biologists, but it is unclear that these findings are relevant to paclitaxel response in patients.
Strengths:
This study identified 53BP1 as a target of CRL3GMCL1-mediated degradation during mitotic arrest. AlphaFold3 predictions of the binding interface, followed by mutational analysis, identified mutants of each protein (GMCL1 R433A and 53BP1 IEDI1422-1425AAAA) that disrupted their interaction. Knock-in of a FLAG tag into the C-terminus of GMCL1 in HCT116 cells, followed by FLAG immunoprecipitation, confirmed that endogenous GMCL1 interacts with endogenous CUL3 and 53BP1 during mitotic arrest.
Weaknesses:
The clinical relevance of the study is overinterpreted. The authors have not taken relevant data about the clinical mechanism of taxanes into account. Supraphysiologic doses of microtubule poisons cause mitotic arrest and can activate the mitotic stopwatch. However, in physiologic concentrations of clinically useful microtubule poisons, cells proceed through mitosis and divide their chromosomes on mitotic spindles that are at least transiently multipolar. Though these low concentrations may result in a brief mitotic delay, it is substantially shorter than the arrest caused by high concentrations of microtubule poisons, and the one mimicked here by 16 hours of 0.4 mg/mL nocodazole, which is not used clinically and does not induce multipolar spindles. Resistance to mitotic arrest occurs through different mechanisms than resistance to multipolar spindles. No evidence is presented in the current version of the manuscript that GMCL1 affects cellular response to clinically relevant doses of paclitaxel.
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Author response:
The following is the authors’ response to the original reviews
Public Reviews:
Reviewer #1 (Public review):
Summary:
Mackie and colleagues compare chemosensory preferences between C. elegans and P. pacificus, and the cellular and molecular mechanisms underlying them. The nematodes have overlapping and distinct preferences for different salts. Although P. pacificus lacks the lsy-6 miRNA important for establishing asymmetry of the left/right ASE salt-sensing neurons in C. elegans, the authors find that P. pacificus ASE homologs achieve molecular (receptor expression) and functional (calcium response) asymmetry by alternative means. This work contributes an important comparison of how these two nematodes sense salts and highlights that evolution can find different ways to establish asymmetry in small nervous systems to optimize the processing of chemosensory cues in the environment.
Strengths:
The authors use clear and established methods to record the response of neurons to chemosensory cues. They were able to show clearly that ASEL/R are functionally asymmetric in P. pacificus, and combined with genetic perturbation establish a role for che-1-dependent gcy-22.3 in in the asymmetric response to NH<sub>4</sub>Cl.
Weaknesses:
The mechanism of lsy-6-independent establishment of ASEL/R asymmetry in P. pacificus remains uncharacterized.
We thank the reviewer for recognizing the novel contributions of our work in revealing the existence of alternative pathways for establishing neuronal lateral asymmetry without the lsy-6 miRNA in a divergent nematode species. We are certainly encouraged now to search for genetic factors that alter the exclusive asymmetric expression of gcy-22.3.
Reviewer #2 (Public review):
Summary:
In this manuscript, Mackie et al. investigate gustatory behavior and the neural basis of gustation in the predatory nematode Pristionchus pacificus. First, they show that the behavioral preferences of P. pacificus for gustatory cues differ from those reported for C. elegans. Next, they investigate the molecular mechanisms of salt sensing in P. pacificus. They show that although the C. elegans transcription factor gene che-1 is expressed specifically in the ASE neurons, the P. pacificus che-1 gene is expressed in the Ppa-ASE and Ppa-AFD neurons. Moreover, che-1 plays a less critical role in salt chemotaxis in P. pacificus than C. elegans. Chemogenetic silencing of Ppa-ASE and Ppa-AFD neurons results in more severe chemotaxis defects. The authors then use calcium imaging to show that both Ppa-ASE and Ppa-AFD neurons respond to salt stimuli. Calcium imaging experiments also reveal that the left and right Ppa-ASE neurons respond differently to salts, despite the fact that P. pacificus lacks lsy-6, a microRNA that is important for ASE left/right asymmetry in C. elegans. Finally, the authors show that the receptor guanylate cyclase gene Ppa-gcy-23.3 is expressed in the right Ppa-ASE neuron (Ppa-ASER) but not the left Ppa-ASE neuron (Ppa-ASEL) and is required for some of the gustatory responses of Ppa-ASER, further confirming that the Ppa-ASE neurons are asymmetric and suggesting that Ppa-GCY-23.3 is a gustatory receptor. Overall, this work provides insight into the evolution of gustation across nematode species. It illustrates how sensory neuron response properties and molecular mechanisms of cell fate determination can evolve to mediate species-specific behaviors. However, the paper would be greatly strengthened by a direct comparison of calcium responses to gustatory cues in C. elegans and P. pacificus, since the comparison currently relies entirely on published data for C. elegans, where the imaging parameters likely differ. In addition, the conclusions regarding Ppa-AFD neuron function would benefit from additional confirmation of AFD neuron identity. Finally, how prior salt exposure influences gustatory behavior and neural activity in P. pacificus is not discussed.
Strengths:
(1) This study provides exciting new insights into how gustatory behaviors and mechanisms differ in nematode species with different lifestyles and ecological niches. The results from salt chemotaxis experiments suggest that P. pacificus shows distinct gustatory preferences from C. elegans. Calcium imaging from Ppa-ASE neurons suggests that the response properties of the ASE neurons differ between the two species. In addition, an analysis of the expression and function of the transcription factor Ppa-che-1 reveals that mechanisms of ASE cell fate determination differ in C. elegans and P. pacificus, although the ASE neurons play a critical role in salt sensing in both species. Thus, the authors identify several differences in gustatory system development and function across nematode species.
(2) This is the first calcium imaging study of P. pacificus, and it offers some of the first insights into the evolution of gustatory neuron function across nematode species.
(3) This study addresses the mechanisms that lead to left/right asymmetry in nematodes. It reveals that the ASER and ASEL neurons differ in their response properties, but this asymmetry is achieved by molecular mechanisms that are at least partly distinct from those that operate in C. elegans. Notably, ASEL/R asymmetry in P. pacificus is achieved despite the lack of a P. pacificus lsy-6 homolog.
Weaknesses:
(1) The authors observe only weak attraction of C. elegans to NaCl. These results raise the question of whether the weak attraction observed is the result of the prior salt environment experienced by the worms. More generally, this study does not address how prior exposure to gustatory cues shapes gustatory responses in P. pacificus. Is salt sensing in P. pacificus subject to the same type of experience-dependent modulation as salt sensing in C. elegans?
We tested if starving animals in the presence of a certain salt will result in those animals avoiding it. However, under our experimental conditions we were unable to detect experiencedependent modulation either in P. pacificus or in C. elegans.
Author response image 1.
(2) A key finding of this paper is that the Ppa-CHE-1 transcription factor is expressed in the PpaAFD neurons as well as the Ppa-ASE neurons, despite the fact that Ce-CHE-1 is expressed specifically in Ce-ASE. However, additional verification of Ppa-AFD neuron identity is required. Based on the image shown in the manuscript, it is difficult to unequivocally identify the second pair of CHE-1-positive head neurons as the Ppa-AFD neurons. Ppa-AFD neuron identity could be verified by confocal imaging of the CHE-1-positive neurons, co-expression of Ppa-che1p::GFP with a likely AFD reporter, thermotaxis assays with Ppa-che-1 mutants, and/or calcium imaging from the putative Ppa-AFD neurons.
In the revised manuscript, we provide additional and, we believe, conclusive evidence for our correct identification of Ppa-AFD neuron being another CHE-1 expressing neuron. Specifically, we have constructed and characterized 2 independent reporter strains of Ppa-ttx-1, a putative homolog of the AFD terminal selector in C. elegans. There are two pairs of ttx-1p::rfp expressing amphid neurons. The anterior neuronal pair have finger-like endings that are unique for AFD neurons compared to the dendritic endings of the 11 other amphid neuron pairs (no neuron type has a wing morphology in P. pacificus). Their cell bodies are detected in the newly tagged TTX-1::ALFA strain that co-localize with the anterior pair of che-1::gfp-expressing amphid neurons (n=15, J2-Adult).
We note that the identity of the posterior pair of amphid neurons differs between the ttx-1p::rfp promoter fusion reporter and TTX-1::ALFA strains– the ttx-1p::rfp posterior amphid pair overlaps with the gcy-22.3p::gfp reporter (ASER) but the TTX-1::ALFA posterior amphid pair do not overlap with the posterior pair of che-1::gfp-expressing amphid neurons (n=15). Given that there are 4 splice forms detected by RNAseq (Transcriptome Assembly Trinity, 2016; www.pristionchus.org), this discrepancy between the Ppa-ttx-1 promoter fusion reporter and the endogenous expression of the Ppa-TTX-1 C-terminally tagged to the only splice form containing Exon 18 (ppa_stranded_DN30925_c0_g1_i5, the most 3’ exon) may be due to differential expression of different splice variants in AFD, ASE, and another unidentified amphid neuron types.
Although we also made reporter strains of two putative AFD markers, Ppa-gcy-8.1 (PPA24212)p::gfp; csuEx101 and Ppa-gcy-8.2 (PPA41407)p::gfp; csuEx100, neither reporter showed neuronal expression.
(3) Loss of Ppa-che-1 causes a less severe phenotype than loss of Ce-che-1. However, the loss of Ppa-che-1::RFP expression in ASE but not AFD raises the question of whether there might be additional start sites in the Ppa-che-1 gene downstream of the mutation sites. It would be helpful to know whether there are multiple isoforms of Ppa-che-1, and if so, whether the exon with the introduced frameshift is present in all isoforms and results in complete loss of Ppa-CHE-1 protein.
According to www.pristionchus.org (Transcriptome Assembly Trinity), there is only a single detectable splice form by RNAseq. Once we have a Ppa-AFD-specific marker, we would be able to determine how much of the AFD terminal effector identify (e.g. expression of gcy-8 paralogs) is effected by the loss of Ppa-che-1 function.
(4) The authors show that silencing Ppa-ASE has a dramatic effect on salt chemotaxis behavior. However, these data lack control with histamine-treated wild-type animals, with the result that the phenotype of Ppa-ASE-silenced animals could result from exposure to histamine dihydrochloride. This is an especially important control in the context of salt sensing, where histamine dihydrochloride could alter behavioral responses to other salts.
We have inadvertently left out this important control. Because the HisCl1 transgene is on a randomly segregating transgene array, we have scored worms with and without the transgene expressing the co-injection marker (Ppa-egl-20p::rfp, a marker in the tail) to show that the presence of the transgene is necessary for the histamine-dependent knockdown of NH<sub>4</sub>Br attraction. This control is added as Figure S2.
(5) The calcium imaging data in the paper suggest that the Ppa-ASE and Ce-ASE neurons respond differently to salt solutions. However, to make this point, a direct comparison of calcium responses in C. elegans and P. pacificus using the same calcium indicator is required. By relying on previously published C. elegans data, it is difficult to know how differences in growth conditions or imaging conditions affect ASE responses. In addition, the paper would be strengthened by additional quantitative analysis of the calcium imaging data. For example, the paper states that 25 mM NH<sub>4</sub>Cl evokes a greater response in ASEL than 250 mM NH<sub>4</sub>Cl, but a quantitative comparison of the maximum responses to the two stimuli is not shown.
We understand that side-by-side comparisons with C. elegans using the same calcium indicator would lend more credence to the differences we observed in P. pacificus versus published findings in C. elegans from the past decades, but are not currently in a position to conduct these experiments in parallel.
(6) It would be helpful to examine, or at least discuss, the other P. pacificus paralogs of Ce-gcy22. Are they expressed in Ppa-ASER? How similar are the different paralogs? Additional discussion of the Ppa-gcy-22 gene expansion in P. pacificus would be especially helpful with respect to understanding the relatively minor phenotype of the Ppa-gcy-22.3 mutants.
In P. pacificus, there are 5 gcy-22-like paralogs and 3 gcy-7-like paralogs, which together form a subclade that is clearly distinct from the 1-1 Cel-gcy-22, Cel-gcy-5, and Cel-gcy-7 orthologs in a phylogenetic tree containing all rGCs in P. pacificus, C. elegans, and C. briggssae (Hong et al, eLife, 2019). In Ortiz et al (2006 and 2009), Cel-gcy-22 stands out from other ASER-type gcy genes (gcy-1, gcy-4, gcy-5) in being located on a separate chromosome (Chr. V) as well as in having a wider range of defects in chemoattraction towards salt ions. Given that the 5 P. pacificus gcy-22-like paralogs are located on 3 separate chromosomes without clear synteny to their C. elegans counterparts, it is likely that the gcy-22 paralogs emerged from independent and repeated gene duplication events after the separation of these Caenorhabditis and Pristionchus lineages. Our reporter strains for two other P. pacificus gcy-22-like paralogs either did not exhibit expression in amphid neurons (Ppa-gcy-22.1p::GFP, ) or exhibited expression in multiple neuron types in addition to a putative ASE neuron (Ppa-gcy-22.4p::GFP). We have expanded the discussion on the other P. pacificus gcy-22 paralogs.
(7) The calcium imaging data from Ppa-ASE is quite variable. It would be helpful to discuss this variability. It would also be helpful to clarify how the ASEL and ASER neurons are being conclusively identified during calcium imaging.
For each animal, the orientation of the nose and vulva were recorded and used as a guide to determine the ventral and dorsal sides of the worm, and subsequently, the left and right sides of the worm. Accounting for the plane of focus of the neuron pairs as viewed through the microscope, it was then determined whether the imaged neuron was the worm’s left or right neuron of each pair. We added this explanation to the Methods.
(8) More information about how the animals were treated prior to calcium imaging would be helpful. In particular, were they exposed to salt solutions prior to imaging? In addition, the animals are in an M9 buffer during imaging - does this affect calcium responses in Ppa-ASE and Ppa-AFD? More information about salt exposure, and how this affects neuron responses, would be very helpful.
Prior to calcium imaging, animals were picked from their cultivation plates (using an eyelash pick to minimize bacteria transfer) and placed in loading solution (M9 buffer with 0.1% Tween20 and 1.5 mM tetramisole hydrochloride, as indicated in the Method) to immobilize the animals until they were visibly completely immobilized.
(9) In Figure 6, the authors say that Ppa-gcy-22.3::GFP expression is absent in the Ppa-che1(ot5012) mutant. However, based on the figure, it looks like there is some expression remaining. Is there a residual expression of Ppa-gcy-22.3::GFP in ASE or possibly ectopic expression in AFD? Does Ppa-che-1 regulate rGC expression in AFD? It would be helpful to address the role of Ppa-che-1 in AFD neuron differentiation.
In Figure 6C, the green signal is autofluorescence in the gut, and there is no GFP expression detected in any of the 55 che-1(-) animals we examined. We are currently developing AFDspecific rGC markers (gcy-8 homologs) to be able to examine the role of Ppa-CHE-1 in regulating AFD identity.
Recommendations for the authors:
Reviewer #1 (Recommendations for the authors):
(1) Abstract: 'how does sensory diversity prevail within this neuronal constraint?' - could be clearer as 'numerical constraint' or 'neuron number constraint'.
We have clarified this passage as ‘…constraint in neuron number’.
(2) 'Sensory neurons in the Pristionchus pacificus' - should get rid of the 'the'.
We have removed the ‘the’.
(3) Figure 2: We have had some good results with the ALFA tag using a similar approach (tagging endogenous loci using CRISPR). I'm not sure if it is a Pristionchus thing, or if it is a result of our different protocols, but our staining appears stronger with less background. We use an adaptation of the Finney-Ruvkin protocol, which includes MeOH in the primary fixation with PFA, and overcomes the cuticle barrier with some LN2 cracking, DTT, then H2O2. No collagenase. If you haven't tested it already it might be worth comparing the next time you have a need for immunostaining.
We appreciate this suggestion. Our staining protocol uses paraformaldehyde fixation. We observed consistent and clear staining in only 4 neurons in CHE-1::ALFA animals but more background signals from TTX-1::ALFA in Figure 2I-J in that could benefit from improved immunostaining protocol.
(4) Page 6: 'By crossing the che-1 reporter transgene into a che-1 mutant background (see below), we also found that che-1 autoregulates its own expression (Figure 2F), as it does in C. elegans' - it took me some effort to understand this. It might make it easier for future readers if this is explained more clearly.
We understand this confusion and have changed the wording along with a supporting table with a more detailed account of che-1p::RFP expression in both ASE and AFD neurons in wildtype and che-1(-) backgrounds in the Results.
(5) Line numbers would make it easier for reviewers to reference the text.
We have added line numbers.
(6) Page 7: is 250mM NH<sub>4</sub>Cl an ecologically relevant concentration? When does off-target/nonspecific activation of odorant receptors become an issue? Some discussion of this could help readers assess the relevance of the salt concentrations used.
This is a great question but one that is difficult to reconcile between experimental conditions that often use 2.5M salt as point-source to establish salt gradients versus ecologically relevant concentrations that are very heterogenous in salinity. Efforts to show C. elegans can tolerate similar levels of salinity between 0.20-0.30 M without adverse effects have been recorded previously (Hu et al., Analytica Chimica Acta 2015; Mah et al. Expedition 2017).
(7) It would be nice for readers to have a short orientation to the ecological relevance of the different salts - e.g. why Pristionchus has a particular taste for ammonium salts.
Pristionchus species are entomophilic and most frequently found to be associated with beetles in a necromenic manner. Insect cadavers could thus represent sources of ammonium in the soil. Additionally, ammonium salts could represent a biological signature of other nematodes that the predatory morphs of P. pacificus could interpret as prey. We have added the possible ecological relevance of ammonium salts into the Discussion.
(8) Page 11: 'multiple P. pacificus che-1p::GCaMP strains did not exhibit sufficient basal fluorescence to allow for image tracking and direct comparison'. 500ms exposure to get enough signal from RCaMP is slow, but based on the figures it still seems enough to capture things. If image tracking was the issue, then using GCaMP6s with SL2-RFP or similar in conjunction with a beam splitter enables tracking when the GCaMP signal is low. Might be an option for the future.
These are very helpful suggestions and we hope to eventually develop an improved che1p::GCaMP strain for future studies.
(9) Sometimes C. elegans genes are referred to as 'C. elegans [gene name]' and sometimes 'Cel [gene name]'. Should be consistent. Same with Pristionchus.
We have now combed through and corrected the inconsistencies in nomenclature.
(10) Pg 12 - '...supports the likelihood that AFD receives inputs, possibly neuropeptidergic, from other amphid neurons' - the neuropeptidergic part could do with some justification.
Because the AFD neurons are not exposed directly to the environment through the amphid channel like the ASE and other amphid neurons, the calcium responses to salts detected in the AFD likely originate from sensory neurons connected to the AFD. However, because there is no synaptic connection from other amphid neurons to the AFD neurons in P. pacificus (unlike in C. elegans; Hong et al, eLife, 2019), it is likely that neuropeptides connect other sensory neurons to the AFDs. To avoid unnecessary confusion, we have removed “possibly neuropeptidergic.”
(11) Pg16: the link to the Hallam lab codon adaptor has a space in the middle. Also, the paper should be cited along with the web address (Bryant and Hallam, 2021).
We have now added the proper link, plus in-text citation. https://hallemlab.shinyapps.io/Wild_Worm_Codon_Adapter/ (Bryant and Hallem, 2021)
Full citation:
Astra S Bryant, Elissa A Hallem, The Wild Worm Codon Adapter: a web tool for automated codon adaptation of transgenes for expression in non-Caenorhabditis nematodes, G3 Genes|Genomes|Genetics, Volume 11, Issue 7, July 2021, jkab146, https://doi.org/10.1093/g3journal/jkab146
Reviewer #2 (Recommendations for the authors):
(1) In Figure 1, the legend states that the population tested was "J4/L4 larvae and young adult hermaphrodites," whereas in the main text, the population was described as "adult hermaphrodites." Please clarify which ages were tested.
We have tested J4-Adult stage hermaphrodites and have made the appropriate corrections in the text.
(2) The authors state that "in contrast to C. elegans, we find that P. pacificus is only moderately and weakly attracted to NaCl and LiCl, respectively." However, this statement does not reflect the data shown in Figure 1, where there is no significant difference between C. elegans and P. pacificus - both species show at most weak attraction to NaCl.
Although there is no statistically significant difference in NaCl attraction between P. pacificus and C. elegans, NaCl attraction in P. pacificus is significantly lower than its attraction to all 3 ammonium salts when compared to C. elegans. We have rephrased this statement as relative differences in the Results and updated the Figure legend.
(3) In Figure 1, the comparisons between C. elegans and P. pacificus should be made using a two-way ANOVA rather than multiple t-tests. Also, the sample sizes should be stated (so the reader does not need to count the circles) and the error bars should be defined.
We performed the 2-way ANOVA to detect differences between C. elegans and P. pacificus for the same salt and between salts within each species. We also indicated the sample size on the figure and defined the error bars.
Significance:
For comparisons of different salt responses within the same species:
- For C. elegans, NH<sub>4</sub>Br vs NH<sub>4</sub>Cl (**p<0.01), NH<sub>4</sub>Cl vs NH<sub>4</sub>I (* p<0.05), and NH<sub>4</sub>Cl vs NaCl (* p<0.05). All other comparisons are not significant.
- For P. pacificus, all salts showed (****p<0.0001) when compared to NaAc and to NH<sub>4</sub>Ac, except for NH<sub>4</sub>Ac and NaAc compared to each other (ns). Also, NH<sub>4</sub>Cl showed (*p<0.05) and NH<sub>4</sub>I showed (***p<0.001) when compared with LiCl and NaCl. All other comparisons are not significant.
For comparisons of salt responses between different species (N2 vs PS312):
- NH<sub>4</sub>I and LiCl (*p<0.05); NaAc and NH<sub>4</sub>Ac (****p<0.0001)
(4) It might be worth doing a power analysis on the data in Figure 3B. If the data are underpowered, this might explain why there is a difference in NH<sub>4</sub>Br response with one of the null mutants but not the other.
For responses to NH<sub>4</sub>Cl, since both che-1 mutants (rather than just one) showed significant difference compared to wildtype, we conducted a power analysis based on the effect size of that difference (~1.2; large). Given this effect size, the sample size for future experiments should be 12 (ANOVA).
For responses to NH<sub>4</sub>Br and given the effect size of the difference seen between wildtype (PS312) and ot5012 (~0.8; large), the sample size for future experiments should be 18 (ANOVA) for a power value of 0.8. Therefore, it is possible that the sample size of 12 for the current experiment was too small to detect a possible difference between the ot5013 alleles and wildtype.
(5) It would be helpful to discuss why silencing Ppa-ASE might result in a switch from attractive to repulsive responses to some of the tested gustatory cues.
For similar assays using Ppa-odr-3p::HisCl1, increasing histamine concentration led to decreasing C.I. for a given odorant (myristate, a P. pacificus-specific attractant). It is likely that the amount of histamine treatment for knockdown to zero (i.e. without a valence change) will differ depending on the attractant.
(6) The statistical tests used in Figure 3 are not stated.
Figure 3 used Two-way ANOVA with Dunnett’s post hoc test. We have now added the test in the figure legend.
(7) It would be helpful to examine the responses of ASER to the full salt panel in the Ppa-gcy-22.3 vs. wild-type backgrounds.
We understand that future experiments examining neuron responses to the full salt panel for wildtype and gcy-22.3 mutants would provide further information about the salts and specific ions associated with the GCY-22.3 receptor. However, we have tested a broader range of salts (although not yet the full panel) for behavioral assays in wildtype vs gcy-22.3 mutants, which we have included as part of an added Figure 8.
(8) The controls shown in Figure S1 may not be adequate. Ideally, the same sample size would be used for the control, allowing differences between control worms and experimental worms to be quantified.
Although we had not conducted an equal number of negative controls using green light without salt stimuli due to resource constraints (6 control vs ~10-19 test), we provided individual recordings with stimuli to show that conditions we interpreted as having responses rarely showed responses resembling the negative controls. Similarly, those we interpreted as having no responses to stimuli mostly resembled the no-stimuli controls (e.g. WT to 25 mM NH<sub>4</sub>Cl, gcy22.3 mutant to 250 mM NH<sub>4</sub>Cl).
(9) An osmolarity control would be helpful for the calcium imaging experiments.
We acknowledge that future calcium imaging experiments featuring different salt concentrations could benefit from osmolarity controls.
(10) In Figure S7, more information about the microfluidic chip design is needed.
The chip design features a U-shaped worm trap to facilitate loading the worm head-first, with a tapered opening to ensure the worm fits snugly and will not slide too far forward during recording. The outer two chip channels hold buffer solution and can be switched open (ON) or closed (OFF) by the Valvebank. The inner two chip channels hold experimental solutions. The inner channel closer to the worm trap holds the control solution, and the inner channel farther from the worm trap holds the stimulant solution.
We have added an image of the chip in Figure S7 and further description in the legend.
(11) Throughout the manuscript, the discussion of the salt stimuli focuses on the salts more than the ions. More discussion of which ions are eliciting responses (both behavioral and neuronal responses) would be helpful.
In Figure 7, the gcy-22.3 defect resulted in a statistically significant reduction in response only towards NH<sub>4</sub>Cl but not towards NaCl, which suggests ASER is the primary neuron detecting NH<sub>4</sub><sup>+</sup> ions. To extend the description of the gcy-22.3 mutant defects to other ions, we have added a Figure 8: chemotaxis on various salt backgrounds. We found only a mild increase in attraction towards NH<sub>4</sub><sup>+</sup> by both gcy-22.3 mutant alleles, but wild-type in their responses toward Cl<sup>-</sup>, Na<sup>+</sup>, or I<sup>-</sup>. The switch in the direction of change between the behavioral (enhanced) and calcium imaging result (reduced) suggests the behavioral response to ammonium ions likely involves additional receptors and neurons.
Minor comments:
(1) The full species name of "C. elegans" should be written out upon first use.
We have added ‘Caenorhabditis elegans’ to its first mention.
(2) In the legend of Figure 1, "N2" should not be in italics.
We have made the correction.
(3) The "che-1" gene should be in lowercase, even when it is at the start of the sentence.
We have made the correction.
(4) Throughout the manuscript, "HisCl" should be "HisCl1."
We have made these corrections to ‘HisCl1’.
(5) Figure 3A would benefit from more context, such as the format seen in Figure 7A. It would also help to have more information in the legend (e.g., blue boxes are exons, etc.).
(6) "Since NH<sub>4</sub>I sensation is affected by silencing of che-1(+) neurons but is unaffected in che-1 mutants, ASE differentiation may be more greatly impacted by the silencing of ASE than by the loss of che-1": I don't think this is exactly what the authors mean. I would say, "ASE function may be more greatly impacted...".
We have changed ‘differentiation’ to ‘function’ in this passage.
(7) In Figure 7F-G, the AFD neurons are referred to as AFD in the figure title but AM12 in the graph. This is confusing.
Thank you for noticing this oversight. We have corrected “AM12” to “AFD”.
(8) In Figure 7, the legend suggests that comparisons within the same genotype were analyzed. I do not see these comparisons in the figure. In which cases were comparisons within the same genotype made?
Correct, we performed additional tests between ON and OFF states within the same genotypes (WT and mutant) but did not find significant differences. To avoid unnecessary confusion, we have removed this sentence.
(9) The nomenclature used for the transgenic animals is unconventional. For example, normally the calcium imaging line would be listed as csuEx93[Ppa-che-1p::optRCaMP] instead of Ppache-1p::optRCaMP(csuEx93).
We have made these corrections to the nomenclature.
(10) Figure S6 appears to come out of order. Also, it would be nice to have more of a legend for this figure. The format of the figure could also be improved for clarity.
We have corrected Figure S6 (now S8) and added more information to the legend.
(11) Methods section, Chemotaxis assays: "Most assays lasted ~3.5 hours at room temperature in line with the speed of P. pacificus without food..." It's not clear what this means. Does it take the worms 3.5 hours to crawl across the surface of the plate?
Correct, P. pacificus requires 3-4 hours to crawl across the surface of the plate, which is the standard time for chemotaxis assays for some odors and all salts. We have added this clarification to the Methods.
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www.youtube.com www.youtube.com
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3:43 wir haben jetzt den Beginn der Massenarbeitlosigkeit, und das war in jeder einzelnen Revolution immer die allerwichtigste Komponente, weil wenn die Leute nichts mehr zu essen haben und sich auch nicht mehr ihr Netflix Abo leisten können, dann gehen sie auf die Straße. diese Rekordsarbeitslosigkeit, das wird das Todesurteil der neuen Regierung sein, und ab jetzt geht es Berg ab, vor allem es ist ja auch kein Ende in Sicht, jeden Tag haben wir neue Schocknachrichten.
7:29 und deswegen könnte man jetzt sagen, naja die werden schon nicht auf die Straße gehen, die bekommen ja schließlich Bürgergeld und Sozialhilfe, aber nichts da, wie vorher gesagt implodiert jetzt ja gerade alles gleichzeitig, also auch der ganze Staatshaushalt, weil immer mehr Arbeitslose bedeutet auch weniger Steuereinnahmen und immer mehr Sozialkosten, und mit der Geschwindigkeit wie es gerade ansteigt ist das irgendwann nicht mehr zu bezahlen. und wenn unsere "Goldstücke" dann irgendwann kein Geld mehr bekommen dann geht's richtig Ramba Zamba.
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Author Response
The following is the authors’ response to the original reviews.
Public Comments
Reviewer 1
(1) Despite the well-established role of Netrin-1 and UNC5C axon guidance during embryonic commissural axons, it remains unclear which cell type(s) express Netrin-1 or UNC5C in the dopaminergic axons and their targets. For instance, the data in Figure 1F-G and Figure 2 are quite confusing. Does Netrin-1 or UNC5C express in all cell types or only dopamine-positive neurons in these two mouse models? It will also be important to provide quantitative assessments of UNC5C expression in dopaminergic axons at different ages.
Netrin-1 is a secreted protein and in this manuscript we did not examine what cell types express Netrin-1. This question is not the focus of the study and we consider it irrelevant to the main issue we are addressing, which is where in the forebrain regions we examined Netrin-1+ cells are present. As per the reviewer’s request we include below images showing Netrin-1 protein and Netrin-1 mRNA expression in the forebrain. In Figure 1 below, we show a high magnification immunofluorescent image of a coronal forebrain section showing Netrin-1 protein expression.
Author response image 1.
This confocal microscope image shows immunofluorescent staining for Netrin-1 (green) localized around cell nuclei (stained by DAPI in blue). This image was taken from a coronal section of the lateral septum of an adult male mouse. Scale bar = 20µm
In Figures 2 and 3 below we show low and high magnification images from an RNAscope experiment confirming that cells in the forebrain regions examined express Netrin-1 mRNA.
Author response image 2.
This confocal microscope image of a coronal brain section of the medial prefrontal cortex of an adult male mouse shows Netrin-1 mRNA expression (green) and cell nuclei (DAPI, blue). Brain regions are as follows: Cg1: Anterior cingulate cortex 1, DP: dorsopeduncular cortex, fmi: forceps minor of the corpus callosum, IL: Infralimbic Cortex, PrL: Prelimbic Cortex
Author response image 3.
A higher resolution image from the same sample as in Figure 2 shows Netrin-1 mRNA (green) and cell nuclei (DAPI; blue). DP = dorsopeduncular cortex
Regarding UNC5c, this receptor homologue is expressed by dopamine neurons in the rodent ventral tegmental area (Daubaras et al., 2014; Manitt et al., 2010; Phillips et al., 2022). This does not preclude UNC5c expression in other cell types. UNC5c receptors are ubiquitously expressed in the brain throughout development, performing many different developmental functions (Kim and Ackerman, 2011; Murcia-Belmonte et al., 2019; Srivatsa et al., 2014). In this study we are interested in UNC5c expression by dopamine neurons, and particularly by their axons projecting to the nucleus accumbens. We therefore used immunofluorescent staining in the nucleus accumbens, showing UNC5 expression in TH+ axons. This work adds to the study by Manitt et al., 2010, which examined UNC5 expression in the VTA. Manitt et al. used Western blotting to demonstrate that UNC5 expression in VTA dopamine neurons increases during adolescence, as can be seen in the following figure:
References:
Daubaras M, Bo GD, Flores C. 2014. Target-dependent expression of the netrin-1 receptor, UNC5C, in projection neurons of the ventral tegmental area. Neuroscience 260:36–46. doi:10.1016/j.neuroscience.2013.12.007
Kim D, Ackerman SL. 2011. The UNC5C Netrin Receptor Regulates Dorsal Guidance of Mouse Hindbrain Axons. J Neurosci 31:2167–2179. doi:10.1523/jneurosci.5254-10.20110.2011
Manitt C, Labelle-Dumais C, Eng C, Grant A, Mimee A, Stroh T, Flores C. 2010. Peri-Pubertal Emergence of UNC-5 Homologue Expression by Dopamine Neurons in Rodents. PLoS ONE 5:e11463-14. doi:10.1371/journal.pone.0011463
Murcia-Belmonte V, Coca Y, Vegar C, Negueruela S, Romero C de J, Valiño AJ, Sala S, DaSilva R, Kania A, Borrell V, Martinez LM, Erskine L, Herrera E. 2019. A Retino-retinal Projection Guided by Unc5c Emerged in Species with Retinal Waves. Current Biology 29:1149-1160.e4. doi:10.1016/j.cub.2019.02.052
Phillips RA, Tuscher JJ, Black SL, Andraka E, Fitzgerald ND, Ianov L, Day JJ. 2022. An atlas of transcriptionally defined cell populations in the rat ventral tegmental area. Cell Reports 39:110616. doi:10.1016/j.celrep.2022.110616
Srivatsa S, Parthasarathy S, Britanova O, Bormuth I, Donahoo A-L, Ackerman SL, Richards LJ, Tarabykin V. 2014. Unc5C and DCC act downstream of Ctip2 and Satb2 and contribute to corpus callosum formation. Nat Commun 5:3708. doi:10.1038/ncomms4708
(2) Figure 1 used shRNA to knockdown Netrin-1 in the Septum and these mice were subjected to behavioral testing. These results, again, are not supported by any valid data that the knockdown approach actually worked in dopaminergic axons. It is also unclear whether knocking down Netrin-1 in the septum will re-route dopaminergic axons or lead to cell death in the dopaminergic neurons in the substantia nigra pars compacta?
First we want to clarify and emphasize, that our knockdown approach was not designed to knock down Netrin-1 in dopamine neurons or their axons. Our goal was to knock down Netrin-1 expression in cells expressing this guidance cue gene in the dorsal peduncular cortex.
We have previously established the efficacy of the shRNA Netrin-1 knockdown virus used in this experiment for reducing the expression of Netrin-1 (Cuesta et al., 2020). The shRNA reduces Netrin-1 levels in vitro and in vivo.
We agree that our experiments do not address the fate of the dopamine axons that are misrouted away from the medial prefrontal cortex. This research is ongoing, and we have now added a note regarding this to our manuscript.
Our current hypothesis, based on experiments being conducted as part of another line of research in the lab, is that these axons are rerouted to a different brain region which they then ectopically innervate. In these experiments we are finding that male mice exposed to tetrahydrocannabinol in adolescence show reduced dopamine innervation in the medial prefrontal cortex in adulthood but increased dopamine input in the orbitofrontal cortex. In addition, these mice show increased action impulsivity in the Go/No-Go task in adulthood (Capolicchio et al., Society for Neuroscience 2023 Abstracts)
References:
Capolicchio T., Hernandez, G., Dube, E., Estrada, K., Giroux, M., Flores, C. (2023) Divergent outcomes of delta 9 - tetrahydrocannabinol in adolescence on dopamine and cognitive development in male and female mice. Society for Neuroscience, Washington, DC, United States [abstract].
Cuesta S, Nouel D, Reynolds LM, Morgunova A, Torres-Berrío A, White A, Hernandez G, Cooper HM, Flores C. 2020. Dopamine Axon Targeting in the Nucleus Accumbens in Adolescence Requires Netrin-1. Frontiers Cell Dev Biology 8:487. doi:10.3389/fcell.2020.00487
(3) Another issue with Figure1J. It is unclear whether the viruses were injected into a WT mouse model or into a Cre-mouse model driven by a promoter specifically expresses in dorsal peduncular cortex? The authors should provide evidence that Netrin-1 mRNA and proteins are indeed significantly reduced. The authors should address the anatomic results of the area of virus diffusion to confirm the virus specifically infected the cells in dorsal peduncular cortex.
All the virus knockdown experiments were conducted in wild type mice, we added this information to Figure 1k.
The efficacy of the shRNA in knocking down Netrin-1 was demonstrated by Cuesta et al. (2020) both in vitro and in vivo, as we show in our response to the reviewer’s previous comment above.
We also now provide anatomical images demonstrating the localization of the injection and area of virus diffusion in the mouse forebrain. In Author response image 4 below the area of virus diffusion is visible as green fluorescent signal.
Author response image 4.
Fluorescent microscopy image of a mouse forebrain demonstrating the localization of the injection of a virus to knock down Netrin-1. The location of the virus is in green, while cell nuclei are in blue (DAPI). Abbreviations: DP: dorsopeduncular cortex IL: infralimbic cortex
References:
Cuesta S, Nouel D, Reynolds LM, Morgunova A, Torres-Berrío A, White A, Hernandez G, Cooper HM, Flores C. 2020. Dopamine Axon Targeting in the Nucleus Accumbens in Adolescence Requires Netrin-1. Frontiers Cell Dev Biology 8:487. doi:10.3389/fcell.2020.00487
(4) The authors need to provide information regarding the efficiency and duration of knocking down. For instance, in Figure 1K, the mice were tested after 53 days post injection, can the virus activity in the brain last for such a long time?
In our study we are interested in the role of Netrin-1 expression in the guidance of dopamine axons from the nucleus accumbens to the medial prefrontal cortex. The critical window for these axons leaving the nucleus accumbens and growing to the cortex is early adolescence (Reynolds et al., 2018b). This is why we injected the virus at the onset of adolescence, at postnatal day 21. As dopamine axons grow from the nucleus accumbens to the prefrontal cortex, they pass through the dorsal peduncular cortex. We disrupted Netrin-1 expression at this point along their route to determine whether it is the Netrin-1 present along their route that guides these axons to the prefrontal cortex. We hypothesized that the shRNA Netrin-1 virus would disrupt the growth of the dopamine axons, reducing the number of axons that reach the prefrontal cortex and therefore the number of axons that innervate this region in adulthood.
We conducted our behavioural tests during adulthood, after the critical window during which dopamine axon growth occurs, so as to observe the enduring behavioral consequences of this misrouting. This experimental approach is designed for the shRNa Netrin-1 virus to be expressed in cells in the dorsopeduncular cortex when the dopamine axons are growing, during adolescence.
References:
Capolicchio T., Hernandez, G., Dube, E., Estrada, K., Giroux, M., Flores, C. (2023) Divergent outcomes of delta 9 - tetrahydrocannabinol in adolescence on dopamine and cognitive development in male and female mice. Society for Neuroscience, Washington, DC, United States [abstract].
Reynolds LM, Yetnikoff L, Pokinko M, Wodzinski M, Epelbaum JG, Lambert LC, Cossette M-P, Arvanitogiannis A, Flores C. 2018b. Early Adolescence is a Critical Period for the Maturation of Inhibitory Behavior. Cerebral cortex 29:3676–3686. doi:10.1093/cercor/bhy247
(5) In Figure 1N-Q, silencing Netrin-1 results in less DA axons targeting to infralimbic cortex, but why the Netrin-1 knocking down mice revealed the improved behavior?
This is indeed an intriguing finding, and we have now added a mention of it to our manuscript. We have demonstrated that misrouting dopamine axons away from the medial prefrontal cortex during adolescence alters behaviour, but why this improves their action impulsivity ability is something currently unknown to us. One potential answer is that the dopamine axons are misrouted to a different brain region that is also involved in controlling impulsive behaviour, perhaps the dorsal striatum (Kim and Im, 2019) or the orbital prefrontal cortex (Jonker et al., 2015).
We would also like to note that we are finding that other manipulations that appear to reroute dopamine axons to unintended targets can lead to reduced action impulsivity as measured using the Go No Go task. As we mentioned above, current experiments in the lab, which are part of a different line of research, are showing that male mice exposed to tetrahydrocannabinol in adolescence show reduced dopamine innervation in the medial prefrontal cortex in adulthood, but increased dopamine input in the orbitofrontal cortex. In addition, these mice show increased action impulsivity in the Go/No-Go task in adulthood (Capolicchio et al., Society for Neuroscience 2023 Abstracts)
References
Capolicchio T., Hernandez, G., Dube, E., Estrada, K., Giroux, M., Flores, C. (2023) Divergent outcomes of delta 9 - tetrahydrocannabinol in adolescence on dopamine and cognitive development in male and female mice. Society for Neuroscience, Washington, DC, United States [abstract].
Jonker FA, Jonker C, Scheltens P, Scherder EJA. 2015. The role of the orbitofrontal cortex in cognition and behavior. Rev Neurosci 26:1–11. doi:10.1515/revneuro2014-0043 Kim B, Im H. 2019. The role of the dorsal striatum in choice impulsivity. Ann N York Acad Sci 1451:92–111. doi:10.1111/nyas.13961
(6) What is the effect of knocking down UNC5C on dopamine axons guidance to the cortex?
We have found that mice that are heterozygous for a nonsense Unc5c mutation, and as a result have reduced levels of UNC5c protein, show reduced amphetamine-induced locomotion and stereotypy (Auger et al., 2013). In the same manuscript we show that this effect only emerges during adolescence, in concert with the growth of dopamine axons to the prefrontal cortex. This is indirect but strong evidence that UNC5c receptors are necessary for correct adolescent dopamine axon development.
References
Auger ML, Schmidt ERE, Manitt C, Dal-Bo G, Pasterkamp RJ, Flores C. 2013. unc5c haploinsufficient phenotype: striking similarities with the dcc haploinsufficiency model. European Journal of Neuroscience 38:2853–2863. doi:10.1111/ejn.12270
(7) In Figures 2-4, the authors only showed the amount of DA axons and UNC5C in NAcc. However, it remains unclear whether these experiments also impact the projections of dopaminergic axons to other brain regions, critical for the behavioral phenotypes. What about other brain regions such as prefrontal cortex? Do the projection of DA axons and UNC5c level in cortex have similar pattern to those in NAcc?
UNC5c receptors are expressed throughout development and are involved in many developmental processes (Kim and Ackerman, 2011; Murcia-Belmonte et al., 2019; Srivatsa et al., 2014). We cannot say whether the pattern we observe here is unique to the nucleus accumbens, but it is certainly not universal throughout the brain.
The brain region we focus on in our manuscript, in addition to the nucleus accumbens, is the medial prefrontal cortex. Close and thorough examination of the prefrontal cortices of adult mice revealed practically no UNC5c expression by dopamine axons. However, we did observe very rare cases of dopamine axons expressing UNC5c. It is not clear whether these rare cases are present before or during adolescence.
Below is a representative set of images of this observation, which is now also included as Supplementary Figure 4:
Author response image 5.
Expression of UNC5c protein in the medial prefrontal cortex of an adult male mouse. Low (A) and high (B) magnification images demonstrate that there is little UNC5c expression in dopamine axons in the medial prefrontal cortex. Here we identify dopamine axons by immunofluorescent staining for tyrosine hydroxylase (TH, see our response to comment #9 regarding the specificity of the TH antibody for dopamine axons in the prefrontal cortex). This figure is also included as Supplementary Figure 4 in the manuscript. Abbreviations: fmi: forceps minor of the corpus callosum, mPFC: medial prefrontal cortex.
References:
Kim D, Ackerman SL. 2011. The UNC5C Netrin Receptor Regulates Dorsal Guidance of Mouse Hindbrain Axons. J Neurosci 31:2167–2179. doi:10.1523/jneurosci.5254- 10.20110.2011
Murcia-Belmonte V, Coca Y, Vegar C, Negueruela S, Romero C de J, Valiño AJ, Sala S, DaSilva R, Kania A, Borrell V, Martinez LM, Erskine L, Herrera E. 2019. A Retino-retinal Projection Guided by Unc5c Emerged in Species with Retinal Waves. Current Biology 29:1149-1160.e4. doi:10.1016/j.cub.2019.02.052
Srivatsa S, Parthasarathy S, Britanova O, Bormuth I, Donahoo A-L, Ackerman SL, Richards LJ, Tarabykin V. 2014. Unc5C and DCC act downstream of Ctip2 and Satb2 and contribute to corpus callosum formation. Nat Commun 5:3708. doi:10.1038/ncomms4708
(8) Can overexpression of UNC5c or Netrin-1 in male winter hamsters mimic the observations in summer hamsters? Or overexpression of UNC5c in female summer hamsters to mimic the winter hamster? This would be helpful to confirm the causal role of UNC5C in guiding DA axons during adolescence.
This is an excellent question. We are very interested in both increasing and decreasing UNC5c expression in hamster dopamine axons to see if we can directly manipulate summer hamsters into winter hamsters and vice versa. We are currently exploring virus-based approaches to design these experiments and are excited for results in this area.
(9) The entire study relied on using tyrosine hydroxylase (TH) as a marker for dopaminergic axons. However, the expression of TH (either by IHC or IF) can be influenced by other environmental factors, that could alter the expression of TH at the cellular level.
This is an excellent point that we now carefully address in our methods by adding the following:
In this study we pay great attention to the morphology and localization of the fibres from which we quantify varicosities to avoid counting any fibres stained with TH antibodies that are not dopamine fibres. The fibres that we examine and that are labelled by the TH antibody show features indistinguishable from the classic features of cortical dopamine axons in rodents (Berger et al., 1974; 1983; Van Eden et al., 1987; Manitt et al., 2011), namely they are thin fibres with irregularly-spaced varicosities, are densely packed in the nucleus accumbens, sparsely present only in the deep layers of the prefrontal cortex, and are not regularly oriented in relation to the pial surface. This is in contrast to rodent norepinephrine fibres, which are smooth or beaded in appearance, relatively thick with regularly spaced varicosities, increase in density towards the shallow cortical layers, and are in large part oriented either parallel or perpendicular to the pial surface (Berger et al., 1974; Levitt and Moore, 1979; Berger et al., 1983; Miner et al., 2003). Furthermore, previous studies in rodents have noted that only norepinephrine cell bodies are detectable using immunofluorescence for TH, not norepinephrine processes (Pickel et al., 1975; Verney et al., 1982; Miner et al., 2003), and we did not observe any norepinephrine-like fibres.
Furthermore, we are not aware of any other processes in the forebrain that are known to be immunopositive for TH under any environmental conditions.
To reduce confusion, we have replaced the abbreviation for dopamine – DA – with TH in the relevant panels in Figures 1, 2, 3, and 4 to clarify exactly what is represented in these images. As can be seen in these images, fluorescent green labelling is present only in axons, which is to be expected of dopamine labelling in these forebrain regions.
References:
Berger B, Tassin JP, Blanc G, Moyne MA, Thierry AM (1974) Histochemical confirmation for dopaminergic innervation of the rat cerebral cortex after destruction of the noradrenergic ascending pathways. Brain Res 81:332–337.
Berger B, Verney C, Gay M, Vigny A (1983) Immunocytochemical Characterization of the Dopaminergic and Noradrenergic Innervation of the Rat Neocortex During Early Ontogeny. In: Proceedings of the 9th Meeting of the International Neurobiology Society, pp 263–267 Progress in Brain Research. Elsevier.
Levitt P, Moore RY (1979) Development of the noradrenergic innervation of neocortex. Brain Res 162:243–259.
Manitt C, Mimee A, Eng C, Pokinko M, Stroh T, Cooper HM, Kolb B, Flores C (2011) The Netrin Receptor DCC Is Required in the Pubertal Organization of Mesocortical Dopamine Circuitry. J Neurosci 31:8381–8394.
Miner LH, Schroeter S, Blakely RD, Sesack SR (2003) Ultrastructural localization of the norepinephrine transporter in superficial and deep layers of the rat prelimbic prefrontal cortex and its spatial relationship to probable dopamine terminals. J Comp Neurol 466:478–494.
Pickel VM, Joh TH, Field PM, Becker CG, Reis DJ (1975) Cellular localization of tyrosine hydroxylase by immunohistochemistry. J Histochem Cytochem 23:1–12.
Van Eden CG, Hoorneman EM, Buijs RM, Matthijssen MA, Geffard M, Uylings HBM (1987) Immunocytochemical localization of dopamine in the prefrontal cortex of the rat at the light and electron microscopical level. Neurosci 22:849–862.
Verney C, Berger B, Adrien J, Vigny A, Gay M (1982) Development of the dopaminergic innervation of the rat cerebral cortex. A light microscopic immunocytochemical study using anti-tyrosine hydroxylase antibodies. Dev Brain Res 5:41–52.
(10) Are Netrin-1/UNC5C the only signal guiding dopamine axon during adolescence? Are there other neuronal circuits involved in this process?
Our intention for this study was to examine the role of Netrin-1 and its receptor UNC5C specifically, but we do not suggest that they are the only molecules to play a role. The process of guiding growing dopamine axons during adolescence is likely complex and we expect other guidance mechanisms to also be involved. From our previous work we know that the Netrin-1 receptor DCC is critical in this process (Hoops and Flores, 2017; Reynolds et al., 2023). Several other molecules have been identified in Netrin-1/DCC signaling processes that control corpus callosum development and there is every possibility that the same or similar molecules may be important in guiding dopamine axons (Schlienger et al., 2023).
References:
Hoops D, Flores C. 2017. Making Dopamine Connections in Adolescence. Trends in Neurosciences 1–11. doi:10.1016/j.tins.2017.09.004
Reynolds LM, Hernandez G, MacGowan D, Popescu C, Nouel D, Cuesta S, Burke S, Savell KE, Zhao J, Restrepo-Lozano JM, Giroux M, Israel S, Orsini T, He S, Wodzinski M, Avramescu RG, Pokinko M, Epelbaum JG, Niu Z, Pantoja-Urbán AH, Trudeau L-É, Kolb B, Day JJ, Flores C. 2023. Amphetamine disrupts dopamine axon growth in adolescence by a sex-specific mechanism in mice. Nat Commun 14:4035. doi:10.1038/s41467-023-39665-1
Schlienger S, Yam PT, Balekoglu N, Ducuing H, Michaud J-F, Makihara S, Kramer DK, Chen B, Fasano A, Berardelli A, Hamdan FF, Rouleau GA, Srour M, Charron F. 2023. Genetics of mirror movements identifies a multifunctional complex required for Netrin-1 guidance and lateralization of motor control. Sci Adv 9:eadd5501. doi:10.1126/sciadv.add5501
(11) Finally, despite the authors' claim that the dopaminergic axon project is sensitive to the duration of daylight in the hamster, they never provided definitive evidence to support this hypothesis.
By “definitive evidence” we think that the reviewer is requesting a single statistical model including measures from both the summer and winter groups. Such a model would provide a probability estimate of whether dopamine axon growth is sensitive to daylight duration. Therefore, we ran these models, one for male hamsters and one for female hamsters.
In both sexes we find a significant effect of daylength on dopamine innervation, interacting with age. Male age by daylength interaction: F = 6.383, p = 0.00242. Female age by daylength interaction: F = 21.872, p = 1.97 x 10-9. The full statistical analysis is available as a supplement to this letter (Response_Letter_Stats_Details.docx).
Reviewer 3
(1) Fig 1 A and B don't appear to be the same section level.
The reviewer is correct that Fig 1B is anterior to Fig 1A. We have changed Figure 1A to match the section level of Figure 1B.
(2) Fig 1C. It is not clear that these axons are crossing from the shell of the NAC.
We have added a dashed line to Figure 1C to highlight the boundary of the nucleus accumbens, which hopefully emphasizes that there are fibres crossing the boundary. We also include here an enlarged image of this panel:
Author response image 6.
An enlarged image of Figure1c in the manuscript. The nucleus accumbens (left of the dotted line) is densely packed with TH+ axons (in green). Some of these TH+ axons can be observed extending from the nucleus accumbens medially towards a region containing dorsally oriented TH+ fibres (white arrows).
(3) Fig 1. Measuring width of the bundle is an odd way to measure DA axon numbers. First the width could be changing during adult for various reasons including change in brain size. Second, I wouldn't consider these axons in a traditional bundle. Third, could DA axon counts be provided, rather than these proxy measures.
With regards to potential changes in brain size, we agree that this could have potentially explained the increased width of the dopamine axon pathway. That is why it was important for us to use stereology to measure the density of dopamine axons within the pathway. If the width increased but no new axons grew along the pathway, we would have seen a decrease in axon density from adolescence to adulthood. Instead, our results show that the density of axons remained constant.
We agree with the reviewer that the dopamine axons do not form a traditional “bundle”. Therefore, throughout the manuscript we now avoid using the term bundle.
Although we cannot count every single axon, an accurate estimate of this number can be obtained using stereology, an unbiassed method for efficiently quantifying large, irregularly distributed objects. We used stereology to count TH+ axons in an unbiased subset of the total area occupied by these axons. Unbiased stereology is the gold-standard technique for estimating populations of anatomical objects, such as axons, that are so numerous that it would be impractical or impossible to measure every single one. Here and elsewhere we generally provide results as densities and areas of occupancy (Reynolds et al., 2022). To avoid confusion, we now clarify that we are counting the width of the area that dopamine axons occupy (rather than the dopamine axon “bundle”).
References:
Reynolds LM, Pantoja-Urbán AH, MacGowan D, Manitt C, Nouel D, Flores C. 2022. Dopaminergic System Function and Dysfunction: Experimental Approaches. Neuromethods 31–63. doi:10.1007/978-1-0716-2799-0_2
(4) TH in the cortex could also be of noradrenergic origin. This needs to be ruled out to score DA axons
This is the same comment as Reviewer 1 #9. Please see our response below, which we have also added to our methods:
In this study we pay great attention to the morphology and localization of the fibres from which we quantify varicosities to avoid counting any fibres stained with TH antibodies that are not dopamine fibres. The fibres that we examine and that are labelled by the TH antibody show features indistinguishable from the classic features of cortical dopamine axons in rodents (Berger et al., 1974; 1983; Van Eden et al., 1987; Manitt et al., 2011), namely they are thin fibres with irregularly-spaced varicosities, are densely packed in the nucleus accumbens, sparsely present only in the deep layers of the prefrontal cortex, and are not regularly oriented in relation to the pial surface. This is in contrast to rodent norepinephrine fibres, which are smooth or beaded in appearance, relatively thick with regularly spaced varicosities, increase in density towards the shallow cortical layers, and are in large part oriented either parallel or perpendicular to the pial surface (Berger et al., 1974; Levitt and Moore, 1979; Berger et al., 1983; Miner et al., 2003). Furthermore, previous studies in rodents have noted that only norepinephrine cell bodies are detectable using immunofluorescence for TH, not norepinephrine processes (Pickel et al., 1975; Verney et al., 1982; Miner et al., 2003), and we did not observe any norepinephrine-like fibres.
References:
Berger B, Tassin JP, Blanc G, Moyne MA, Thierry AM (1974) Histochemical confirmation for dopaminergic innervation of the rat cerebral cortex after destruction of the noradrenergic ascending pathways. Brain Res 81:332–337.
Berger B, Verney C, Gay M, Vigny A (1983) Immunocytochemical Characterization of the Dopaminergic and Noradrenergic Innervation of the Rat Neocortex During Early Ontogeny. In: Proceedings of the 9th Meeting of the International Neurobiology Society, pp 263–267 Progress in Brain Research. Elsevier.
Levitt P, Moore RY (1979) Development of the noradrenergic innervation of neocortex. Brain Res 162:243–259.
Manitt C, Mimee A, Eng C, Pokinko M, Stroh T, Cooper HM, Kolb B, Flores C (2011) The Netrin Receptor DCC Is Required in the Pubertal Organization of Mesocortical Dopamine Circuitry. J Neurosci 31:8381–8394.
Miner LH, Schroeter S, Blakely RD, Sesack SR (2003) Ultrastructural localization of the norepinephrine transporter in superficial and deep layers of the rat prelimbic prefrontal cortex and its spatial relationship to probable dopamine terminals. J Comp Neurol 466:478–494.
Pickel VM, Joh TH, Field PM, Becker CG, Reis DJ (1975) Cellular localization of tyrosine hydroxylase by immunohistochemistry. J Histochem Cytochem 23:1–12.
Van Eden CG, Hoorneman EM, Buijs RM, Matthijssen MA, Geffard M, Uylings HBM (1987) Immunocytochemical localization of dopamine in the prefrontal cortex of the rat at the light and electron microscopical level. Neurosci 22:849–862.
Verney C, Berger B, Adrien J, Vigny A, Gay M (1982) Development of the dopaminergic innervation of the rat cerebral cortex. A light microscopic immunocytochemical study using anti-tyrosine hydroxylase antibodies. Dev Brain Res 5:41–52.
(5) Netrin staining should be provided with NeuN + DAPI; its not clear these are all cell bodies. An in situ of Netrin would help as well.
A similar comment was raised by Reviewer 1 in point #1. Please see below the immunofluorescent and RNA scope images showing expression of Netrin-1 protein and mRNA in the forebrain.
Author response image 7.
This confocal microscope image shows immunofluorescent staining for Netrin-1 (green) localized around cell nuclei (stained by DAPI in blue). This image was taken from a coronal section of the lateral septum of an adult male mouse. Scale bar = 20µm
Author response image 8.
This confocal microscope image of a coronal brain section of the medial prefrontal cortex of an adult male mouse shows Netrin-1 mRNA expression (green) and cell nuclei (DAPI, blue). RNAscope was used to generate this image. Brain regions are as follows: Cg1: Anterior cingulate cortex 1, DP: dorsopeduncular cortex, IL: Infralimbic Cortex, PrL: Prelimbic Cortex, fmi: forceps minor of the corpus callosum
Author response image 9.
A higher resolution image from the same sample as in Figure 2 shows Netrin-1 mRNA (green) and cell nuclei (DAPI; blue). DP = dorsopeduncular cortex
(6) The Netrin knockdown needs validation. How strong was the knockdown etc?
This comment was also raised by Reviewer 1 #1.
We have previously established the efficacy of the shRNA Netrin-1 knockdown virus used in this experiment for reducing the expression of Netrin-1 (Cuesta et al., 2020). The shRNA reduces Netrin-1 levels in vitro and in vivo.
References:
Cuesta S, Nouel D, Reynolds LM, Morgunova A, Torres-Berrío A, White A, Hernandez G, Cooper HM, Flores C. 2020. Dopamine Axon Targeting in the Nucleus Accumbens in Adolescence Requires Netrin-1. Frontiers Cell Dev Biology 8:487. doi:10.3389/fcell.2020.00487
(7) If the conclusion that knocking down Netrin in cortex decreases DA innervation of the IL, how can that be reconciled with Netrin-Unc repulsion.
This is an intriguing question and one that we are in the planning stages of addressing with new experiments.
Although we do not have a mechanistic answered for how a repulsive receptor helps guide these axons, we would like to note that previous indirect evidence from a study by our group also suggests that reducing UNC5c signaling in dopamine axons in adolescence increases dopamine innervation to the prefrontal cortex (Auger et al, 2013).
References
Auger ML, Schmidt ERE, Manitt C, Dal-Bo G, Pasterkamp RJ, Flores C. 2013. unc5c haploinsufficient phenotype: striking similarities with the dcc haploinsufficiency model. European Journal of Neuroscience 38:2853–2863. doi:10.1111/ejn.12270
(8) The behavioral phenotype in Fig 1 is interesting, but its not clear if its related to DA axons/signaling. IN general, no evidence in this paper is provided for the role of DA in the adolescent behaviors described.
We agree with the reviewer that the behaviours we describe in adult mice are complex and are likely to involve several neurotransmitter systems. However, there is ample evidence for the role of dopamine signaling in cognitive control behaviours (Bari and Robbins, 2013; Eagle et al., 2008; Ott et al., 2023) and our published work has shown that alterations in the growth of dopamine axons to the prefrontal cortex leads to changes in impulse control as measured via the Go/No-Go task in adulthood (Reynolds et al., 2023, 2018a; Vassilev et al., 2021).
The other adolescent behaviour we examined was risk-like taking behaviour in male and female hamsters (Figures 4 and 5), as a means of characterizing maturation in this behavior over time. We decided not to use the Go/No-Go task because as far as we know, this has never been employed in Siberian Hamsters and it will be difficult to implement. Instead, we chose the light/dark box paradigm, which requires no training and is ideal for charting behavioural changes over short time periods. Indeed, risk-like taking behavior in rodents and in humans changes from adolescence to adulthood paralleling changes in prefrontal cortex development, including the gradual input of dopamine axons to this region.
References:
Bari A, Robbins TW. 2013. Inhibition and impulsivity: Behavioral and neural basis of response control. Progress in neurobiology 108:44–79. doi:10.1016/j.pneurobio.2013.06.005
Eagle DM, Bari A, Robbins TW. 2008. The neuropsychopharmacology of action inhibition: cross-species translation of the stop-signal and go/no-go tasks. Psychopharmacology 199:439–456. doi:10.1007/s00213-008-1127-6
Ott T, Stein AM, Nieder A. 2023. Dopamine receptor activation regulates reward expectancy signals during cognitive control in primate prefrontal neurons. Nat Commun 14:7537. doi:10.1038/s41467-023-43271-6
Reynolds LM, Hernandez G, MacGowan D, Popescu C, Nouel D, Cuesta S, Burke S, Savell KE, Zhao J, Restrepo-Lozano JM, Giroux M, Israel S, Orsini T, He S, Wodzinski M, Avramescu RG, Pokinko M, Epelbaum JG, Niu Z, Pantoja-Urbán AH, Trudeau L-É, Kolb B, Day JJ, Flores C. 2023. Amphetamine disrupts dopamine axon growth in adolescence by a sex-specific mechanism in mice. Nat Commun 14:4035. doi:10.1038/s41467-023-39665-1
Reynolds LM, Pokinko M, Torres-Berrío A, Cuesta S, Lambert LC, Pellitero EDC, Wodzinski M, Manitt C, Krimpenfort P, Kolb B, Flores C. 2018a. DCC Receptors Drive Prefrontal Cortex Maturation by Determining Dopamine Axon Targeting in Adolescence. Biological psychiatry 83:181–192. doi:10.1016/j.biopsych.2017.06.009
Vassilev P, Pantoja-Urban AH, Giroux M, Nouel D, Hernandez G, Orsini T, Flores C. 2021. Unique effects of social defeat stress in adolescent male mice on the Netrin-1/DCC pathway, prefrontal cortex dopamine and cognition (Social stress in adolescent vs. adult male mice). Eneuro ENEURO.0045-21.2021. doi:10.1523/eneuro.0045-21.2021
(9) Fig2 - boxes should be drawn on the NAc diagram to indicate sampled regions. Some quantification of Unc5c would be useful. Also, some validation of the Unc5c antibody would be nice.
The images presented were taken medial to the anterior commissure and we have edited Figure 2 to show this. However, we did not notice any intra-accumbens variation, including between the core and the shell. Therefore, the images are representative of what was observed throughout the entire nucleus accumbens.
To quantify UNC5c in the accumbens we conducted a Western blot experiment in male mice at different ages. A one-way ANOVA analyzing band intensity (relative to the 15-day-old average band intensity) as the response variable and age as the predictor variable showed a significant effect of age (F=5.615, p=0.01). Posthoc analysis revealed that 15-day-old mice have less UNC5c in the nucleus accumbens compared to 21- and 35-day-old mice.
Author response image 10.
The graph depicts the results of a Western blot experiment of UNC5c protein levels in the nucleus accumbens of male mice at postnatal days 15, 21 or 35 and reveals a significant increase in protein levels at the onset adolescence.
Our methods for this Western blot were as follows: Samples were prepared as previously (Torres-Berrío et al., 2017). Briefly, mice were sacrificed by live decapitation and brains were flash frozen in heptane on dry ice for 10 seconds. Frozen brains were mounted in a cryomicrotome and two 500um sections were collected for the nucleus accumbens, corresponding to plates 14 and 18 of the Paxinos mouse brain atlas. Two tissue core samples were collected per section, one for each side of the brain, using a 15-gauge tissue corer (Fine surgical tools Cat no. NC9128328) and ejected in a microtube on dry ice. The tissue samples were homogenized in 100ul of standard radioimmunoprecipitation assay buffer using a handheld electric tissue homogenizer. The samples were clarified by centrifugation at 4C at a speed of 15000g for 30 minutes. Protein concentration was quantified using a bicinchoninic acid assay kit (Pierce BCA protein assay kit, Cat no.PI23225) and denatured with standard Laemmli buffer for 5 minutes at 70C. 10ug of protein per sample was loaded and run by SDS-PAGE gel electrophoresis in a Mini-PROTEAN system (Bio-Rad) on an 8% acrylamide gel by stacking for 30 minutes at 60V and resolving for 1.5 hours at 130V. The proteins were transferred to a nitrocellulose membrane for 1 hour at 100V in standard transfer buffer on ice. The membranes were blocked using 5% bovine serum albumin dissolved in tris-buffered saline with Tween 20 and probed with primary (UNC5c, Abcam Cat. no ab302924) and HRP-conjugated secondary antibodies for 1 hour. a-tubulin was probed and used as loading control. The probed membranes were resolved using SuperSignal West Pico PLUS chemiluminescent substrate (ThermoFisher Cat no.34579) in a ChemiDoc MP Imaging system (Bio-Rad). Band intensity was quantified using the ChemiDoc software and all ages were normalized to the P15 age group average.
Validation of the UNC5c antibody was performed in the lab of Dr. Liu, from whom it was kindly provided. Briefly, in the validation study the authors showed that the anti-UNC5C antibody can detect endogenous UNC5C expression and the level of UNC5C is dramatically reduced after UNC5C knockdown. The antibody can also detect the tagged-UNC5C protein in several cell lines, which was confirmed by a tag antibody (Purohit et al., 2012; Shao et al., 2017).
References:
Purohit AA, Li W, Qu C, Dwyer T, Shao Q, Guan K-L, Liu G. 2012. Down Syndrome Cell Adhesion Molecule (DSCAM) Associates with Uncoordinated-5C (UNC5C) in Netrin-1mediated Growth Cone Collapse. The Journal of biological chemistry 287:27126–27138. doi:10.1074/jbc.m112.340174
Shao Q, Yang T, Huang H, Alarmanazi F, Liu G. 2017. Uncoupling of UNC5C with Polymerized TUBB3 in Microtubules Mediates Netrin-1 Repulsion. J Neurosci 37:5620–5633. doi:10.1523/jneurosci.2617-16.2017
(10) "In adolescence, dopamine neurons begin to express the repulsive Netrin-1 receptor UNC5C, and reduction in UNC5C expression appears to cause growth of mesolimbic dopamine axons to the prefrontal cortex".....This is confusing. Figure 2 shows a developmental increase in UNc5c not a decrease. So when is the "reduction in Unc5c expression" occurring?
We apologize for the mistake in this sentence. We have corrected the relevant passage in our manuscript as follows:
In adolescence, dopamine neurons begin to express the repulsive Netrin-1 receptor UNC5C, particularly when mesolimbic and mesocortical dopamine projections segregate in the nucleus accumbens (Manitt et al., 2010; Reynolds et al., 2018a). In contrast, dopamine axons in the prefrontal cortex do not express UNC5c except in very rare cases (Supplementary Figure 4). In adult male mice with Unc5c haploinsufficiency, there appears to be ectopic growth of mesolimbic dopamine axons to the prefrontal cortex (Auger et al., 2013). This miswiring is associated with alterations in prefrontal cortex-dependent behaviours (Auger et al., 2013).
References:
Auger ML, Schmidt ERE, Manitt C, Dal-Bo G, Pasterkamp RJ, Flores C. 2013. unc5c haploinsufficient phenotype: striking similarities with the dcc haploinsufficiency model. European Journal of Neuroscience 38:2853–2863. doi:10.1111/ejn.12270
Manitt C, Labelle-Dumais C, Eng C, Grant A, Mimee A, Stroh T, Flores C. 2010. Peri-Pubertal Emergence of UNC-5 Homologue Expression by Dopamine Neurons in Rodents. PLoS ONE 5:e11463-14. doi:10.1371/journal.pone.0011463
Reynolds LM, Pokinko M, Torres-Berrío A, Cuesta S, Lambert LC, Pellitero EDC, Wodzinski M, Manitt C, Krimpenfort P, Kolb B, Flores C. 2018a. DCC Receptors Drive Prefrontal Cortex Maturation by Determining Dopamine Axon Targeting in Adolescence. Biological psychiatry 83:181–192. doi:10.1016/j.biopsych.2017.06.009
(11) In Fig 3, a statistical comparison should be made between summer male and winter male, to justify the conclusions that the winter males have delayed DA innervation.
This analysis was also suggested by Reviewer 1, #11. Here is our response:
We analyzed the summer and winter data together in ANOVAs separately for males and females. In both sexes we find a significant effect of daylength on dopamine innervation, interacting with age. Male age by daylength interaction: F = 6.383, p = 0.00242. Female age by daylength interaction: F = 21.872, p = 1.97 x 10-9. The full statistical analysis is available as a supplement to this letter (Response_Letter_Stats_Details.docx).
(12) Should axon length also be measured here (Fig 3)? It is not clear why the authors have switched to varicosity density. Also, a box should be drawn in the NAC cartoon to indicate the region that was sampled.
It is untenable to quantify axon length in the prefrontal cortex as we cannot distinguish independent axons. Rather, they are “tangled”; they twist and turn in a multitude of directions as they make contact with various dendrites. Furthermore, they branch extensively. It would therefore be impossible to accurately quantify the number of axons. Using unbiased stereology to quantify varicosities is a valid, well-characterized and straightforward alternative (Reynolds et al., 2022).
References:
Reynolds LM, Pantoja-Urbán AH, MacGowan D, Manitt C, Nouel D, Flores C. 2022. Dopaminergic System Function and Dysfunction: Experimental Approaches. Neuromethods 31–63. doi:10.1007/978-1-0716-2799-0_2
(13) In Fig 3, Unc5c should be quantified to bolster the interesting finding that Unc5c expression dynamics are different between summer and winter hamsters. Unc5c mRNA experiments would also be important to see if similar changes are observed at the transcript level.
We agree that it would be very interesting to see how UNC5c mRNA and protein levels change over time in summer and winter hamsters, both in males, as the reviewer suggests here, and in females. We are working on conducting these experiments in hamsters as part of a broader expansion of our research in this area. These experiments will require a lengthy amount of time and at this point we feel that they are beyond the scope of this manuscript.
(14) Fig 4. The peak in exploratory behavior in winter females is counterintuitive and needs to be better discussed. IN general, the light dark behavior seems quite variable.
This is indeed a very interesting finding, which we have expanded upon in our manuscript as follows:
When raised under a winter-mimicking daylength, hamsters of either sex show a protracted peak in risk taking. In males, it is delayed beyond 80 days old, but the delay is substantially less in females. This is a counterintuitive finding considering that dopamine development in winter females appears to be accelerated. Our interpretation of this finding is that the timing of the risk-taking peak in females may reflect a balance between different adolescent developmental processes. The fact that dopamine axon growth is accelerated does not imply that all adolescent maturational processes are accelerated. Some may be delayed, for example those that induce axon pruning in the cortex. The timing of the risk-taking peak in winter female hamsters may therefore reflect the amalgamation of developmental processes that are advanced with those that are delayed – producing a behavioural effect that is timed somewhere in the middle. Disentangling the effects of different developmental processes on behaviour will require further experiments in hamsters, including the direct manipulation of dopamine activity in the nucleus accumbens and prefrontal cortex.
Full Reference List
Auger ML, Schmidt ERE, Manitt C, Dal-Bo G, Pasterkamp RJ, Flores C. 2013. unc5c haploinsufficient phenotype: striking similarities with the dcc haploinsufficiency model. European Journal of Neuroscience 38:2853–2863. doi:10.1111/ejn.12270
Bari A, Robbins TW. 2013. Inhibition and impulsivity: Behavioral and neural basis of response control. Progress in neurobiology 108:44–79. doi:10.1016/j.pneurobio.2013.06.005
Cuesta S, Nouel D, Reynolds LM, Morgunova A, Torres-Berrío A, White A, Hernandez G, Cooper HM, Flores C. 2020. Dopamine Axon Targeting in the Nucleus Accumbens in Adolescence Requires Netrin-1. Frontiers Cell Dev Biology 8:487. doi:10.3389/fcell.2020.00487
Daubaras M, Bo GD, Flores C. 2014. Target-dependent expression of the netrin-1 receptor, UNC5C, in projection neurons of the ventral tegmental area. Neuroscience 260:36–46. doi:10.1016/j.neuroscience.2013.12.007
Eagle DM, Bari A, Robbins TW. 2008. The neuropsychopharmacology of action inhibition: crossspecies translation of the stop-signal and go/no-go tasks. Psychopharmacology 199:439– 456. doi:10.1007/s00213-008-1127-6
Hoops D, Flores C. 2017. Making Dopamine Connections in Adolescence. Trends in Neurosciences 1–11. doi:10.1016/j.tins.2017.09.004
Jonker FA, Jonker C, Scheltens P, Scherder EJA. 2015. The role of the orbitofrontal cortex in cognition and behavior. Rev Neurosci 26:1–11. doi:10.1515/revneuro-2014-0043
Kim B, Im H. 2019. The role of the dorsal striatum in choice impulsivity. Ann N York Acad Sci 1451:92–111. doi:10.1111/nyas.13961
Kim D, Ackerman SL. 2011. The UNC5C Netrin Receptor Regulates Dorsal Guidance of Mouse Hindbrain Axons. J Neurosci 31:2167–2179. doi:10.1523/jneurosci.5254-10.2011
Manitt C, Labelle-Dumais C, Eng C, Grant A, Mimee A, Stroh T, Flores C. 2010. Peri-Pubertal Emergence of UNC-5 Homologue Expression by Dopamine Neurons in Rodents. PLoS ONE 5:e11463-14. doi:10.1371/journal.pone.0011463
Murcia-Belmonte V, Coca Y, Vegar C, Negueruela S, Romero C de J, Valiño AJ, Sala S, DaSilva R, Kania A, Borrell V, Martinez LM, Erskine L, Herrera E. 2019. A Retino-retinal Projection Guided by Unc5c Emerged in Species with Retinal Waves. Current Biology 29:1149-1160.e4. doi:10.1016/j.cub.2019.02.052
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Reynolds LM, Pokinko M, Torres-Berrío A, Cuesta S, Lambert LC, Pellitero EDC, Wodzinski M, Manitt C, Krimpenfort P, Kolb B, Flores C. 2018a. DCC Receptors Drive Prefrontal Cortex Maturation by Determining Dopamine Axon Targeting in Adolescence. Biological psychiatry 83:181–192. doi:10.1016/j.biopsych.2017.06.009
Reynolds LM, Yetnikoff L, Pokinko M, Wodzinski M, Epelbaum JG, Lambert LC, Cossette M-P, Arvanitogiannis A, Flores C. 2018b. Early Adolescence is a Critical Period for the Maturation of Inhibitory Behavior. Cerebral cortex 29:3676–3686. doi:10.1093/cercor/bhy247
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Vassilev P, Pantoja-Urban AH, Giroux M, Nouel D, Hernandez G, Orsini T, Flores C. 2021. Unique effects of social defeat stress in adolescent male mice on the Netrin-1/DCC pathway, prefrontal cortex dopamine and cognition (Social stress in adolescent vs. adult male mice). Eneuro ENEURO.0045-21.2021. doi:10.1523/eneuro.0045-21.2021
Private Comments
Reviewer #1
(12) The language should be improved. Some expression is confusing (line178-179). Also some spelling errors (eg. Figure 1M).
We have removed the word “Already” to make the sentence in lines 178-179 clearer, however we cannot find a spelling error in Figure 1M or its caption. We have further edited the manuscript for clarity and flow.
Reviewer #2
(1) The authors claim to have revealed how the 'timing of adolescence is programmed in the brain'. While their findings certainly shed light on molecular, circuit and behavioral processes that are unique to adolescence, their claim may be an overstatement. I suggest they refine this statement to discuss more specifically the processes they observed in the brain and animal behavior, rather than adolescence itself.
We agree with the reviewer and have revised the manuscript to specify that we are referring to the timing of specific developmental processes that occur in the adolescent brain, not adolescence overall.
(2) Along the same lines, the authors should also include a more substantiative discussion of how they selected their ages for investigation (for both mice and hamsters), For mice, their definition of adolescence (P21) is earlier than some (e.g. Spear L.P., Neurosci. and Beh. Reviews, 2000).
There are certainly differences of opinion between researchers as to the precise definition of adolescence and the period it encompasses. Spear, 2000, provides one excellent discussion of the challenges related to identifying adolescence across species. This work gives specific ages only for rats, not mice (as we use here), and characterizes post-natal days 28-42 as being the conservative age range of “peak” adolescence (page 419, paragraph 1). Immediately thereafter the review states that the full adolescent period is longer than this, and it could encompass post-natal days 20-55 (page 419, paragraph 2).
We have added the following statement to our methods:
There is no universally accepted way to define the precise onset of adolescence. Therefore, there is no clear-cut boundary to define adolescent onset in rodents (Spear, 2000). Puberty can be more sharply defined, and puberty and adolescence overlap in time, but the terms are not interchangeable. Puberty is the onset of sexual maturation, while adolescence is a more diffuse period marked by the gradual transition from a juvenile state to independence. We, and others, suggest that adolescence in rodents spans from weaning (postnatal day 21) until adulthood, which we take to start on postnatal day 60 (Reynolds and Flores, 2021). We refer to “early adolescence” as the first two weeks postweaning (postnatal days 21-34). These ranges encompass discrete DA developmental periods (Kalsbeek et al., 1988; Manitt et al., 2011; Reynolds et al., 2018a), vulnerability to drug effects on DA circuitry (Hammerslag and Gulley, 2014; Reynolds et al., 2018a), and distinct behavioral characteristics (Adriani and Laviola, 2004; Makinodan et al., 2012; Schneider, 2013; Wheeler et al., 2013).
References:
Adriani W, Laviola G. 2004. Windows of vulnerability to psychopathology and therapeutic strategy in the adolescent rodent model. Behav Pharmacol 15:341–352. doi:10.1097/00008877-200409000-00005
Hammerslag LR, Gulley JM. 2014. Age and sex differences in reward behavior in adolescent and adult rats. Dev Psychobiol 56:611–621. doi:10.1002/dev.21127
Hoops D, Flores C. 2017. Making Dopamine Connections in Adolescence. Trends in Neurosciences 1–11. doi:10.1016/j.tins.2017.09.004
Kalsbeek A, Voorn P, Buijs RM, Pool CW, Uylings HBM. 1988. Development of the Dopaminergic Innervation in the Prefrontal Cortex of the Rat. The Journal of Comparative Neurology 269:58–72. doi:10.1002/cne.902690105
Makinodan M, Rosen KM, Ito S, Corfas G. 2012. A critical period for social experiencedependent oligodendrocyte maturation and myelination. Science 337:1357–1360. doi:10.1126/science.1220845
Manitt C, Mimee A, Eng C, Pokinko M, Stroh T, Cooper HM, Kolb B, Flores C. 2011. The Netrin Receptor DCC Is Required in the Pubertal Organization of Mesocortical Dopamine Circuitry. J Neurosci 31:8381–8394. doi:10.1523/jneurosci.0606-11.2011
Reynolds LM, Flores C. 2021. Mesocorticolimbic Dopamine Pathways Across Adolescence: Diversity in Development. Front Neural Circuit 15:735625. doi:10.3389/fncir.2021.735625
Reynolds LM, Yetnikoff L, Pokinko M, Wodzinski M, Epelbaum JG, Lambert LC, Cossette MP, Arvanitogiannis A, Flores C. 2018. Early Adolescence is a Critical Period for the Maturation of Inhibitory Behavior. Cerebral cortex 29:3676–3686. doi:10.1093/cercor/bhy247
Schneider M. 2013. Adolescence as a vulnerable period to alter rodent behavior. Cell and tissue research 354:99–106. Doi:10.1007/s00441-013-1581-2
Spear LP. 2000. Neurobehavioral Changes in Adolescence. Current directions in psychological science 9:111–114. doi:10.1111/1467-8721.00072
Wheeler AL, Lerch JP, Chakravarty MM, Friedel M, Sled JG, Fletcher PJ, Josselyn SA, Frankland PW. 2013. Adolescent Cocaine Exposure Causes Enduring Macroscale Changes in Mouse Brain Structure. J Neurosci 33:1797–1803. doi:10.1523/jneurosci.3830-12.2013
(3) Figure 1 - the conclusions hinge on the Netrin-1 staining, as shown in panel G, but the cells are difficult to see. It would be helpful to provide clearer, more zoomed images so readers can better assess the staining. Since Netrin-1 expression reduces dramatically after P4 and they had to use antigen retrieval to see signal, it would be helpful to show some images from additional brain regions and ages to see if expression levels follow predicted patterns. For instance, based on the allen brain atlas, it seems that around P21, there should be high levels of Netrin-1 in the cerebellum, but low levels in the cortex. These would be nice controls to demonstrate the specificity and sensitivity of the antibody in older tissue.
We do not study the cerebellum and have never stained this region; doing so now would require generating additional tissue and we’re not sure it would add enough to the information provided to be worthwhile. Note that we have stained the forebrain for Netrin-1 previously, providing broad staining of many brain regions (Manitt et al., 2011)
References:
Manitt C, Mimee A, Eng C, Pokinko M, Stroh T, Cooper HM, Kolb B, Flores C. 2011. The Netrin Receptor DCC Is Required in the Pubertal Organization of Mesocortical Dopamine Circuitry. J Neurosci 31:8381–8394. doi:10.1523/jneurosci.0606-11.2011
(4) Figure 3 - Because mice tend to avoid brightly-lit spaces, the light/dark box is more commonly used as a measure of anxiety-like behavior than purely exploratory behavior (including in the paper they cited). It is important to address this possibility in their discussion of their findings. To bolster their conclusions about the coincidence of circuit and behavioral changes in adolescent hamsters, it would be useful to add an additional measure of exploratory behaviors (e.g. hole board).
Regarding the light/dark box test, this is an excellent point. We prefer the term “risk taking” to “anxiety-like” and now use the former term in our manuscript. Furthermore, our interest in the behaviour is purely to chart the development of adolescent behaviour across our treatment groups, not to study a particular emotional state. Regardless of the specific emotion or emotions governing the light/dark box behaviour, it is an ideal test for charting adolescent shifts in behaviour as it is well-characterized in this respect, as we discuss in our manuscript.
(5) Supplementary Figure 4,5 The authors defined puberty onset using uterine and testes weights in hamsters. While the weights appear to be different for summer and winter hamsters, there were no statistical comparison. Please add statistical analyses to bolster claims about puberty start times. Also, as many studies use vaginal opening to define puberty onset, it would be helpful to discuss how these measurements typically align and cite relevant literature that described use of uterine weights. Also, Supplementary Figures 4 and 5 were mis-cited as Supp. Fig. 2 in the text (e.g. line 317 and others).
These are great suggestions. We have added statistical analyses to Supplementary Figures 5 and 6 and provided Vaginal Opening data as Supplementary Figure 7. The statistical analyses confirm that all three characters are delayed in winter hamsters compared to summer hamsters.
We have also added the following references to the manuscript:
Darrow JM, Davis FC, Elliott JA, Stetson MH, Turek FW, Menaker M. 1980. Influence of Photoperiod on Reproductive Development in the Golden Hamster. Biol Reprod 22:443–450. doi:10.1095/biolreprod22.3.443
Ebling FJP. 1994. Photoperiodic Differences during Development in the Dwarf Hamsters Phodopus sungorus and Phodopus campbelli. Gen Comp Endocrinol 95:475–482. doi:10.1006/gcen.1994.1147
Timonin ME, Place NJ, Wanderi E, Wynne-Edwards KE. 2006. Phodopus campbelli detect reduced photoperiod during development but, unlike Phodopus sungorus, retain functional reproductive physiology. Reproduction 132:661–670. doi:10.1530/rep.1.00019
(6) The font in many figure panels is small and hard to read (e.g. 1A,D,E,H,I,L...). Please increase the size for legibility.
We have increased the font size of our figure text throughout the manuscript.
Reviewer #3
(15) Fig 1 C,D. Clarify the units of the y axis
We have now fixed this.
Full Reference List
Adriani W, Laviola G. 2004. Windows of vulnerability to psychopathology and therapeutic strategy in the adolescent rodent model. Behav Pharmacol 15:341–352. doi:10.1097/00008877-200409000-00005
Hammerslag LR, Gulley JM. 2014. Age and sex differences in reward behavior in adolescent and adult rats. Dev Psychobiol 56:611–621. doi:10.1002/dev.21127
Hoops D, Flores C. 2017. Making Dopamine Connections in Adolescence. Trends in Neurosciences 1–11. doi:10.1016/j.tins.2017.09.004
Kalsbeek A, Voorn P, Buijs RM, Pool CW, Uylings HBM. 1988. Development of the Dopaminergic Innervation in the Prefrontal Cortex of the Rat. The Journal of Comparative Neurology 269:58–72. doi:10.1002/cne.902690105
Makinodan M, Rosen KM, Ito S, Corfas G. 2012. A critical period for social experiencedependent oligodendrocyte maturation and myelination. Science 337:1357–1360. doi:10.1126/science.1220845
Manitt C, Mimee A, Eng C, Pokinko M, Stroh T, Cooper HM, Kolb B, Flores C. 2011. The Netrin Receptor DCC Is Required in the Pubertal Organization of Mesocortical Dopamine Circuitry. J Neurosci 31:8381–8394. doi:10.1523/jneurosci.0606-11.2011
Reynolds LM, Flores C. 2021. Mesocorticolimbic Dopamine Pathways Across Adolescence: Diversity in Development. Front Neural Circuit 15:735625. doi:10.3389/fncir.2021.735625 Reynolds LM, Yetnikoff L, Pokinko M, Wodzinski M, Epelbaum JG, Lambert LC, Cossette M-P, Arvanitogiannis A, Flores C. 2018. Early Adolescence is a Critical Period for the Maturation of Inhibitory Behavior. Cerebral cortex 29:3676–3686. doi:10.1093/cercor/bhy247
Schneider M. 2013. Adolescence as a vulnerable period to alter rodent behavior. Cell and tissue research 354:99–106. doi:10.1007/s00441-013-1581-2
Spear LP. 2000. Neurobehavioral Changes in Adolescence. Current directions in psychological science 9:111–114. doi:10.1111/1467-8721.00072
Wheeler AL, Lerch JP, Chakravarty MM, Friedel M, Sled JG, Fletcher PJ, Josselyn SA, Frankland PW. 2013. Adolescent Cocaine Exposure Causes Enduring Macroscale Changes in Mouse Brain Structure. J Neurosci 33:1797–1803. doi:10.1523/jneurosci.3830-12.2013
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Author Response
The following is the authors’ response to the original reviews.
eLife assessment
This important study combines a range of advanced ultrastructural imaging approaches to define the unusual endosomal system of African trypanosomes. Compelling images show that instead of a distinct set of compartments, the endosome of these protists comprises a continuous system of membranes with functionally distinct subdomains as defined by canonical markers of early, late and recycling endosomes. The findings suggest that the endocytic system of bloodstream stages has evolved to facilitate the extraordinarily high rates of membrane turnover needed to remove immune complexes and survive in the blood, which is of interest to anyone studying infectious diseases.
Public Reviews:
Reviewer #1 (Public Review):
Summary:
Bloodstream stages of the parasitic protist, Trypanosoma brucei, exhibit very high rates of constitutive endocytosis, which is needed to recycle the surface coat of Variant Surface Glycoproteins (VSGs) and remove surface immune complexes. While many studies have shown that the endo-lysosomal systems of T. brucei BF stages contain canonical domains, as defined by classical Rab markers, it has remained unclear whether these protists have evolved additional adaptations/mechanisms for sustaining these very high rates of membrane transport and protein sorting. The authors have addressed this question by reconstructing the 3D ultrastructure and functional domains of the T. brucei BF endosome membrane system using advanced electron tomography and super-resolution microscopy approaches. Their studies reveal that, unusually, the BF endosome network comprises a continuous system of cisternae and tubules that contain overlapping functional subdomains. It is proposed that a continuous membrane system allows higher rates of protein cargo segregation, sorting and recycling than can otherwise occur when transport between compartments is mediated by membrane vesicles or other fusion events.
Strengths:
The study is a technical tour-de-force using a combination of electron tomography, super-resolution/expansion microscopy, immune-EM of cryo-sections to define the 3D structures and connectivity of different endocytic compartments. The images are very clear and generally support the central conclusion that functionally distinct endocytic domains occur within a dynamic and continuous endosome network in BF stages.
Weaknesses:
The authors suggest that this dynamic endocytic network may also fulfil many of the functions of the Golgi TGN and that the latter may be absent in these stages. Although plausible, this comment needs further experimental support. For example, have the authors attempted to localize canonical makers of the TGN (e.g. GRIP proteins) in T. brucei BF and/or shown that exocytic carriers bud directly from the endosomes?
We agree with the criticism and have shortened the discussion accordingly and clearly marked it as speculation. However, we do not want to completely abandon our hypothesis.
The paragraph now reads:
Lines 740 – 751:
“Interestingly, we did not find any structural evidence of vesicular retrograde transport to the Golgi. Instead, the endosomal ‘highways’ extended throughout the posterior volume of the trypanosomes approaching the trans-Golgi interface. It is highly plausible that this region represents the convergence point where endocytic and biosynthetic membrane trafficking pathways merge. A comparable merging of endocytic and biosynthetic functions has been described for the TGN in plants. Different marker proteins for early and recycling endosomes were shown to be associated and/ or partially colocalized with the TGN suggesting its function in both secretory and endocytic pathways (reviewed in Minamino and Ueda, 2019). As we could not find structural evidence for the existence of a TGN we tentatively propose that trypanosomes may have shifted the central orchestrating function of the TGN as a sorting hub at the crossroads of biosynthetic and recycling pathways to the endosome. Although this is a speculative scenario, it is experimentally testable.”
Furthermore, we removed the lines 51 - 52, which included the suggestion of the TGN as a master regulator, from the abstract.
Reviewer #2 (Public Review):
The authors suggest that the African trypanosome endomembrane system has unusual organisation, in that the entire system is a single reticulated structure. It is not clear if this is thought to extend to the lysosome or MVB. There is also a suggestion that this unusual morphology serves as a trans-(post)Golgi network rather than the more canonical arrangement.
The work is based around very high-quality light and electron microscopy, as well as utilising several marker proteins, Rab5A, 11 and 7. These are deemed as markers for early endosomes, recycling endosomes and late or pre-lysosomes. The images are mostly of high quality but some inconsistencies in the interpretation, appearance of structures and some rather sweeping assumptions make this less easy to accept. Two perhaps major issues are claims to label the entire endosomal apparatus with a single marker protein, which is hard to accept as certainly this reviewer does not really even know where the limits to the endosomal network reside and where these interface with other structures. There are several additional compartments that have been defined by Rob proteins as well, and which are not even mentioned. Overall I am unconvinced that the authors have demonstrated the main things they claim.<br /> The endomembrane system in bloodstream form T. brucei is clearly delimited. Compared to mammalian cells it is tidy and confined to the posterior part of the spindleshaped cell. The endoplasmic reticulum is linked to one side of the longitudinal cell axis, marked by the attached flagellum, while the mitochondrion locates to the opposite side. Glycosomes are easily identifiable as spheres, as are acidocalcisomes, which are smaller than glycosomes and – in electron micrographs – are characterized by high electron density. All these organelles extend beyond the nucleus, which is not the case for the endosomal compartment, the lysosome and the Golgi. The vesicles found in the posterior half of the trypanosome cell are quantitatively identifiable as COP1, CCVI or CCVII vesicles, or exocytic carriers. The lysosome has a higher degree of morphological plasticity, but this is not topic of the present work. Thus, the endomembrane system in T. brucei is comparatively well structured and delimited, which is why we have chosen trypanosomes as cell biological model.
We have published EP1::GFP as marker for the endosome system and flagellar pocket back in 2004. We have defined the fluid phase volume of the trypanosome endosome in papers published between 2002 and 2007. This work was not intended to represent the entirety of RAB proteins. We were only interested in 3 canonical markers for endosome subtypes. We do not claim anything that is not experimentally tested, we have clearly labelled our hypotheses as such, and we do not make sweeping assumptions.
The approaches taken are state-of-the-art but not novel, and because of the difficulty in fully addressing the central tenet, I am not sure how much of an impact this will have beyond the trypanosome field. For certain this is limited to workers in the direct area and is not a generalisable finding.
To the best of our knowledge, there is no published research that has employed 3D Tokuyasu or expansion microscopy (ExM) to label endosomes. The key takeaway from our study, which is the concept that "endosomes are continuous in trypanosomes" certainly is novel. We are not aware of any other report that has demonstrated this aspect.
The doubts formulated by the reviewer regarding the impact of our work beyond the field of trypanosomes are not timely. Indeed, our results, and those of others, show that the conclusions drawn from work with just a few model organisms is not generalisable. We are finally on the verge of a new cell biology that considers the plethora of evolutionary solutions beyond ophistokonts. We believe that this message should be widely acknowledged and considered. And we are certainly not the only ones who are convinced that the term "general relevance" is unscientific and should no longer be used in biology.
Reviewer #3 (Public Review):
Summary:
As clearly highlighted by the authors, a key plank in the ability of trypanosomes to evade the mammalian host’s immune system is its high rate of endocytosis. This rapid turnover of its surface enables the trypanosome to ‘clean’ its surface removing antibodies and other immune effectors that are subsequently degraded. The high rate of endocytosis is likely reflected in the organisati’n and layout of the endosomal system in these parasites. Here, Link et al., sought to address this question using a range of light and three-dimensional electron microscopy approaches to define the endosomal organisation in this parasite.
Before this study, the vast majority of our information about the make-up of the trypanosome endosomal system was from thin-section electron microscopy and immunofluorescence studies, which did not provide the necessary resolution and 3D information to address this issue. Therefore, it was not known how the different structures observed by EM were related. Link et al., have taken advantage of the advances in technology and used an impressive combination of approaches at the LM and EM level to study the endosomal system in these parasites. This innovative combination has now shown the interconnected-ness of this network and demonstrated that there are no ‘classical’ compartments within the endosomal system, with instead different regions of the network enriched in different protein markers (Rab5a, Rab7, Rab11).
Strengths:
This is a generally well-written and clear manuscript, with the data well-presented supporting the majority of the conclusions of the authors. The authors use an impressive range of approaches to address the organisation of the endosomal system and the development of these methods for use in trypanosomes will be of use to the wider parasitology community.
I appreciate their inclusion of how they used a range of different light microscopy approaches even though for instance the dSTORM approach did not turn out to be as effective as hoped. The authors have clearly demonstrated that trypanosomes have a large interconnected endosomal network, without defined compartments and instead show enrichment for specific Rabs within this network.
Weaknesses:
My concerns are:
i) There is no evidence for functional compartmentalisation. The classical markers of different endosomal compartments do not fully overlap but there is no evidence to show a region enriched in one or other of these proteins has that specific function. The authors should temper their conclusions about this point.
The reviewer is right in stating that Rab-presence does not necessarily mean Rabfunction. However, this assumption is as old as the Rab literature. That is why we have focused on the 3 most prominent endosomal marker proteins. We report that for endosome function you do not necessarily need separate membrane compartments. This is backed by our experiments.
ii) The quality of the electron microscopy work is very high but there is a general lack of numbers. For example, how many tomograms were examined? How often were fenestrated sheets seen? Can the authors provide more information about how frequent these observations were?
The fenestrated sheets can be seen in the majority of the 37 tomograms recorded of the posterior volume of the parasites. Furthermore, we have randomly generated several hundred tiled (= very large) electron micrographs of bloodstream form trypanosomes for unbiased analyses of endomembranes. In these 2D-datasets the “footprint” of the fenestrated flat and circular cisternae is frequently detectable in the posterior cell area.
We now have included the corresponding numbers in all EM figure legends.
iii) The EM work always focussed on cells which had been processed before fixing. Now, I understand this was important to enable tracers to be used. However, given the dynamic nature of the system these processing steps and feeding experiments may have affected the endosomal organisation. Given their knowledge of the system now, the authors should fix some cells directly in culture to observe whether the organisation of the endosome aligns with their conclusions here.
This is a valid criticism; however, it is the cell culture that provides an artificial environment. As for a possible effect of cell harvesting by centrifugation on the integrity and functionality of the endosome system, we consider this very unlikely for one simple reason. The mechanical forces acting in and on the parasites as they circulate in the extremely crowded and confined environment of the mammalian bloodstream are obviously much higher than the centrifugal forces involved in cell preparation. This becomes particularly clear when one considers that the mass of the particle to be centrifuged determines the actual force exerted by the g-forces. Nevertheless, the proposed experiment is a good control, although much more complex than proposed, since tomography is a challenging technique. We have performed the suggested experiment and acquired tomograms of unprocessed cells. The corresponding data is now included as supplementary movie 2, 3 and 4. We refer to it in lines 202 – 206: To investigate potential impacts of processing steps (cargo uptake, centrifugation, washing) on endosomal organization, we directly fixed cells in the cell culture flask, embedded them in Epon, and conducted tomography. The resulting tomograms revealed endosomal organization consistent with that observed in cells fixed after processing (see Supplementary movie 2, 3, and 4).
We furthermore thank the reviewer for the experiment suggestion in the acknowledgments.
iv) The discussion needs to be revamped. At the moment it is just another run through of the results and does not take an overview of the results presenting an integrated view. Moreover, it contains reference to data that was not presented in the results.
We have improved the discussion accordingly.
Recommendations for the authors:
The reviewers concurred about the high calibre of the work and the importance of the findings.
They raised some issues and made some suggestions to improve the paper without additional experiments - key issues include
(1) Better referencing of the trypanosome endocytosis/ lysosomal trafficking literature.
The literature, especially the experimental and quantitative work, is very limited. We now provide a more complete set of references. However, we would like to mention that we had cited a recent review that critically references the trypanosome literature with emphasis on the extensive work done with mammalian cells and yeast.
(2) Moving the dSTORM data that detracts from otherwise strong data in a supplementary figure.
We have done this.
(3) Removal of the conclusion that the continuous endosome fulfils the functions of TGN, without further evidence.
As stated above, this was not a conclusion in our paper, but rather a speculation, which we have now more clearly marked as such. Lines 740 to 751 now read:
“Interestingly, we did not find any structural evidence of vesicular retrograde transport to the Golgi. Instead, the endosomal ‘highways’ extended throughout the posterior volume of the trypanosomes approaching the trans-Golgi interface. It is highly plausible that this region represents the convergence point where endocytic and biosynthetic membrane trafficking pathways merge. A comparable merging of endocytic and biosynthetic functions was already described for the TGN in plants. Different marker proteins for early and recycling endosomes were shown to be associated and/ or partially colocalized with the TGN suggesting its function in both secretory and endocytic pathways (reviewed in Minamino and Ueda, 2019). As we could not find structural evidence for the existence of a TGN we tentatively propose that trypanosomes may have shifted the central orchestrating function of the TGN as a sorting hub at the crossroads of biosynthetic and recycling pathways to the endosome. Although this is a speculative scenario, it is experimentally testable.”
(4) Broader discussion linking their findings to other examples of organelle maturation in eukaryotes (e.g cisternal maturation of the Golgi)
We have improved the discussion accordingly.
Reviewer #1 (Recommendations For The Authors):
What are the multi-vesicular vesicles that surround the marked endosomal compartments in Fig 1. Do they become labelled with fluid phase markers with longer incubations (e.g late endosome/ lysosomal)?
The function of MVBs in trypanosomes is still far from being clear. They are filled with fluid phase cargo, especially ferritin, but are devoid of VSG. Hence it is likely that MVBs are part of the lysosomal compartment. In fact, this part of the endomembrane system is highly dynamic. MVBs can be physically connected to the lysosome or can form elongated structures. The surprising dynamics of the trypanosome lysosome will be published elsewhere.
Figure 2. The compartments labelled with EP1::Halo are very poorly defined due to the low levels of expression of the reporter protein and/or sensitivity of detection of the Halo tag. Based on these images, it would be hard to conclude whether the endosome network is continuous or not. In this respect, it is unclear why the authors didn't use EP1-GFP for these analyses? Given the other data that provides more compelling evidence for a single continuous compartment, I would suggest removing Fig 2A.
We have used EP1::GFP to label the entire endosome system (Engstler and Boshart, 2004). Unfortunately, GFP is not suited for dSTORM imaging. By creating the EP1::Halo cell line, we were able to utilize the most prominent dSTORM fluorescent dye, Alexa 647. This was not primarily done to generate super resolution images, but rather to measure the dynamics of the GPI-anchored, luminal protein EP with single molecule precision. The results from this study will be published separately. But we agree with the reviewer and have relocated the dSTORM data to the supplementary material.
The observation that Rab5a/7 can be detected in the lumen of lysosome is interesting. Mechanistically, this presumably occurs by invagination of the limiting membrane of the lysosome. Is there any evidence that similar invagination of cytoplasmic markers occurs throughout or in subdomains of the endocytic network (possibly indicative of a 'late endosome' domain)?
So far, we have not observed this. The structure of the lysosome and the membrane influx from the endosome are currently being investigated.
The authors note that continuity of functionally distinct membrane compartments in the secretory/endocytic pathways has been reported in other protists (e.g T. cruzi). A particular example that could be noted is the endo-lysosomal system of Dictyostelium discoideum which mediates the continuous degradation and eventual expulsion of undigested material.
We tried to include this in the discussion but ultimately decided against it because the Dictyostelium system cannot be easily compared to the trypanosome endosome.
Reviewer #2 (Recommendations For The Authors):
Abstract
Not sure that 'common' is the correct term here. Frequent, near-universal..... it would be true that endocytosis is common across most eukaryotes.
We have changed the sentence to “common process observed in most eukaryotes” (line 33).
Immune evasion - the parasite does not escape the immune system, but does successfully avoid its impact, at least at the population level.
We have replaced the word “escape” with “evasion” (line 35).
The third sentence needs to follow on correctly from the second. Also, more than Igs are internalised and potentially part of immune evasion, such as C3, Factor H, ApoL1 etcetera.
We believe that there may be a misunderstanding here. The process of endocytic uptake and lysosomal degradation has so far only been demonstrated in the context of VSGbound antibodies, which is why we only refer to this. Of course, the immune system comprises a wide range of proteins and effector molecules, all of which could be involved in immune evasion.
I do not follow the logic that the high flux through the endocytic system in trypanosomes precludes distinct compartmentalisation - one could imagine a system where a lot of steps become optimised for example. This idea needs expanding on if it is correct.
Membrane transport by vesicle transfer between several separate membrane compartments would be slower than the measured rate of membrane flux.
Again I am not sure 'efficient' on line 40. It is fast, but how do you measure efficiency? Speed and efficiency are not the same thing.
We have replaced the word “efficient” with “fast” (line 42).
The basis for suggesting endosomes as a TGN is unclear. Given that there are AP complexes, retromer, exocyst and other factors that are part of the TGN or at least post-G differentiation of pathways in canonical systems, this seems a step too far. There really is no evidence in the rest of the MS that seems to support this.
Yes, we agree and have clarified the discussion accordingly. We have not completely removed the discussion on the TGN but have labelled it more clearly as speculation.
I am aware I am being pedantic here, but overall the abstract seems to provide an impression of greater novelty than may be the case and makes several very bold claims that I cannot see as fully valid.
We are not aware of any claim in the summary that we have not substantiated with experiments, or any hypothesis that we have not explained.
Moreover, the concept of fused or multifunctional endosomes (or even other endomembrane compartments) is old, and has been demonstrated in metazoan cells and yeast. The concept of rigid (in terms of composition) compartments really has been rejected by most folks with maturation, recycling and domain structures already well-established models and concepts.
We agree that the (transient) presence of multiple Rab proteins decorating endosomes has been demonstrated in various cell types. This finding formed the basis for the endosomal maturation model in mammals and yeast, which has replaced the previous rigid compartment model.
However, we do not appreciate attempts to question the originality of our study by claiming that similar observations have been made in metazoans or yeast. This is simply wrong. There are no reports of a functionally structured, continuous, single and large endosome in any other system. The only membrane system that might be similar was described in the American parasite Trypanosoma cruzi, however, without the use of endosome markers or any functional analysis. We refer to this study in the discussion.
In summary, the maturation model falls short in explaining the intricacies of the membrane system we have uncovered in trypanosomes. Therefore, one plausible interpretation of our data is that the overall architecture of the trypanosome endosomes represents an adaptation that enables the remarkable speed of plasma membrane recycling observed in these parasites. In our view, both our findings and their interpretation are novel and worth reporting. Again, modern cell biology should recognize that evolution has developed many solutions for similar processes in cells, about whose diversity we have learned almost nothing because of our reductionist view. A remarkable example of this are the Picozoa, tiny bipartite eukaryotes that pack the entire nutritional apparatus into one pouch and the main organelles with the locomotor system into the other. Another one is the “extreme” cell biology of many protozoan parasites such as Giardia, Toxpoplasma or Trypanosoma.
Higher plants have been well characterised, especially at the level of Rab/Arf proteins and adaptins.
We now mention plant endosomes in our brief discussion of the trypanosome TGN. Lines 744 – 747:
“A comparable merging of endocytic and biosynthetic functions was already described for the TGN in plants. Different marker proteins for early and recycling endosomes were shown to be associated and/ or partially colocalized with the TGN suggesting its function in both secretory and endocytic pathways (reviewed in Minamino and Ueda, 2019).”
The level of self-citing in the introduction is irritating and unscholarly. I have no qualms with crediting the authors with their own excellent contributions, but work from Dacks, Bangs, Field and others seems to be selectively ignored, with an awkward use of the authors' own publications. Diversity between organisms for example has been a mainstay of the Dacks lab output, Rab proteins and others from Field and work on exocytosis and late endosomal systems from Bangs. These efforts and contributions surely deserve some recognition?
This is an original article and not a review. For a comprehensive overview the reviewer might read our recent overview article on exo- and endocytic pathways in trypanosomes, in which we have extensively cited the work of Mark Field, Jay Bangs and Joel Dacks. In the present manuscript, we have cited all papers that touch on our results or are otherwise important for a thorough understanding of our hypotheses. We do not believe that this approach is unscientific, but rather improves the readability of the manuscript. Nevertheless, we have now cited additional work.
For the uninitiated, the posterior/anterior axis of the trypanosome cell as well as any other specific features should be defined.
In lines 102 - 110 we wrote:
“This process of antibody clearance is driven by hydrodynamic drag forces resulting from the continuous directional movement of trypanosomes (Engstler et al., 2007). The VSG-antibody complexes on the cell surface are dragged against the swimming direction of the parasite and accumulate at the posterior pole of the cell. This region harbours an invagination in the plasma membrane known as the flagellar pocket (FP) (Gull, 2003; Overath et al., 1997). The FP, which marks the origin of the single attached flagellum, is the exclusive site for endo- and exocytosis in trypanosomes (Gull, 2003; Overath et al., 1997). Consequently, the accumulation of VSG-antibody complexes occurs precisely in the area of bulk membrane uptake.”
We think this sufficiently introduces the cell body axes.
I don't understand the comment concerning microtubule association. In mammalian cells, such association is well established, but compartments still do not display precise positioning. This likely then has nothing to do with the microtubule association differences.
We have clarified this in the text (lines 192 – 199). There is no report of cytoplasmic microtubules in trypanosomes. All microtubules appear to be either subpellicular or within the flagellum. To maintain the structure and position of the endosomal apparatus, they should be associated either with subpellicular microtubules, as is the case with the endoplasmic reticulum, or with the more enigmatic actomyosin system of the parasites. We have been working on the latter possibility and intend to publish a follow-up paper to the present manuscript.
The inability to move past the nucleus is a poor explanation. These compartments are dynamic. Even the nucleus does interesting things in trypanosomes and squeezes past structures during development in the tsetse fly.
The distance between the nucleus and the microtubule cytoskeleton remains relatively constant even in parasites that squeeze through microfluidic channels. This is not unexpected as the nucleus can be highly deformed. A structure the size of the endosome will not be able to physically pass behind the nucleus without losing its integrity. In fact, the recycling apparatus is never found in the anterior part of the trypanosome, most probably because the flagellar pocket is located at the posterior cell pole.
L253 What is the evidence that EP1 labels the entire FP and endosomes? This may be extensive, but this claim requires rather more evidence. This is again suggested at l263. Again, please forgive me for being pedantic, but this is an overstatement unless supported by evidence that would be incredibly difficult to obtain. This is even sort of acknowledged on l271 in the context of non-uniform labelling. This comes again in l336.
The evidence that EP1 labels the entire FP and endosomes is presented here: Engstler and Boshart, 2004; 10.1101/gad.323404).
Perhaps I should refrain from comments on the dangers of expansion microscopy, or asking what has actually been gained here. Oddly, the conclusion on l290 is a fair statement that I am happy with.
An in-depth discussion regarding the advantages and disadvantages of expansion microscopy is beyond the manuscript's intended scope. Our approach involved utilizing various imaging techniques to confirm the validity of our findings. We appreciate that our concluding sentence is pleasing.
F2 - The data in panel A seem quite poor to me. I also do not really understand why the DAPI stain in the first and second columns fails to coincide or why the kinetoplast is so diffuse in the second row. The labelling for EP1 presents as very small puncta, and hence is not evidence for a continuum. What is the arrow in A IV top? The data in panel B are certainly more in line with prior art, albeit that there is considerable heterogeneity in the labelling and of the FP for example. Again, I cannot really see this as evidence for continuity. There are gaps.... Albeit I accept that labelling of such structures is unlikely to ever be homogenous.
We agree that the dSTORM data represents the least robust aspect of the findings we have presented, and we concur with relocating it to the supplementary material.
F3 - Rather apparent, and specifically for Rab7, that there is differential representation - for example, Cell 4 presents a single Rab7 structure while the remaining examples demonstrate more extensive labelling. Again, I am content that these are highly dynamic strictures but this needs to be addressed at some level and commented upon. If the claim is for continuity, the dynamics observed here suggest the usual; some level of obvious overlap of organellar markers, but the representation in F3 is clever but not sure what I am looking at. Moreover, the title of the figure is nothing new. What is also a bit odd is that the extent of the Rab7 signal, and to some extent the other two Rabs used, is rather variable, which makes this unclear to me as to what is being detected. Given that the Rab proteins may be defining microdomains or regions, I would also expect a region of unique straining as well as the common areas. This needs to at least be discussed.
The differences in the representation result from the dynamics of the labelled structures. Therefore, we have selected different cells to provide examples of what the labelling can look like. We now mention this in the results section.
The overlap of the different Rab signals was perhaps to be expected, but we now have demonstrated it experimentally. Importantly, we performed a rigorous quantification by calculating the volume overlaps and the Pearson correlation coefficients.
In previous studies the data were presented as maximal intensity projections, which inherently lack the complete 3D information.
We found that Rab proteins define microdomains and that there are regions of unique staining as well as common areas, as shown in Figure 3. The volumes do not completely overlap. This is now more clearly stated in lines 315 – 319:
“These objects showed areas of unique staining as well as partially overlapping regions. The pairwise colocalization of different endosomal markers is shown in Figure 3 A, XI - XIII and 3 B. The different cells in Figure 3 B were selected to represent the dynamic nature of the labelled structures. Consequently, the selected cells provide a variety of examples of how the labelling can appear.”
This had already been stated in lines 331 – 336:
“In summary, the quantitative colocalization analyses revealed that on the one hand, the endosomal system features a high degree of connectivity, with considerable overlap of endosomal marker regions, and on the other hand, TbRab5A, TbRab7, and TbRab11 also demarcate separated regions in that system. These results can be interpreted as evidence of a continuous endosomal membrane system harbouring functional subdomains, with a limited amount of potentially separated early, late or recycling endosomes.”
F4-6 - Fabulous images. But a couple of issues here; first, as the authors point out, there is distance between the gold and the antigen. So, this of course also works in the z-plane as well as the x/y-planes and some of the gold may well be associated with membraneous figures that are out of the plane, which would indicate an absence of colinearity on one specific membrane. Secondly, in several instances, we have Rab7 essentially mixed with Rab11 or Rab5 positive membrane. While data are data and should be accepted, this is difficult to reconcile when, at least to some level, Rab7 is a marker for a late-endosomal structure and where the presence of degradative activity could reside. As division of function is, I assume, the major reason for intracellular compartmentalisation, such a level of admixture is hard to rationalise. A continuum is one thing but the data here seem to be suggesting something else, i.e. almost complete admixture.
We are grateful for the positive feedback regarding the image quality. It is true that the "linkage error," representing the distance between the gold and the antigen, also functions to some extent in the z-axis. However, it's important to note that the zdimension of the section in these Figures is 55 nm. Nevertheless, it's interesting to observe that membranes, which may not be visible within the section itself but likely the corresponding Rab antigen, is discernible in Figure 4C (indicated by arrows).
We have clarified this in lines 397 – 400:
“Consequently, gold particles located further away may represent cytoplasmic TbRab proteins or, as the “linkage error” can also occur in the z-plane, correspond to membranes that are not visible within the 55 nm thickness of the cryosection (Figure 4, panel C, arrows). “
The coexistence of different Rabs is most likely concentrated in regions where transitions between different functions are likely. Our focus was primarily on imaging membranes labelled with two markers. We wanted to show that the prevailing model of separate compartments in the trypanosome literature is not correct.
F7 - Not sure what this adds beyond what was published by Grunfelder.
First, this figure is an important control that links our results to published work (Grünfelder et al. (2003)). Second, we include double staining of cargo with Rab5, Rab7, and Rab11, whereas Grünfelder focused only on Rab11. Therefore, our data is original and of such high quality that it warrants a main figure.
F8 - and l583. This is odd as the claim is 'proof' which in science is a hard thing to claim (and this is definitely not at a six sigma level of certainty, as used by the physics community). However, I am seeing structures in the tomograms which are not contiguous - there are gaps here between the individual features (Green in the figure).
We have replaced the term "proof". It is important to note that the structures in individual tomograms cannot all be completely continuous because the sections are limited to a thickness of 250 nm. Therefore, it is likely that they have more connectivity above and below the imaged section. Nevertheless, we believe that the quality of the tomograms is satisfactory, considering that 3D Tokuyasu is a very demanding technique and the production of serial Tokuyasu tomograms is not feasible in practice.
Discussion - Too long and the self-citing of four papers from the corresponding author to the exclusion of much prior work is again noted, with concerns about this as described above. Moreover, at least four additional Rab proteins are known associated with the trypanosome endosomal system, 4, 5B, 21 and 28. These have been completely ignored.
We have outlined our position on referencing in original articles above. We also explained why we focused on the key marker proteins associated with early (Rab5), late (Rab7) and recycling endosomes (Rab11). We did not ignore the other Rabs, we just did not include them in the present study.
Overall this is disappointing. I had expected a more robust analysis, with a clearer discussion and placement in context. I am not fully convinced that what we have here is as extreme as claimed, or that we have a substantial advance. There is nothing here that is mechanistic or the identification of a new set of gene products, process or function.
We do not think that this is constructive feedback.
This MS suggests that the endosomal system of African trypanosomes is a continuum of membrane structures rather than representing a set of distinct compartments. A combination of light and electron microscopy methods are used in support. The basic contention is very challenging to prove, and I'm not convinced that this has been. Furthermore, I am also unclear as to the significance of such an organisation; this seems not really addressed.
We acknowledge and respect varying viewpoints, but we hold a differing perspective in this matter. We are convinced that the data decisively supports our interpretation. May future work support or refute our hypothesis.
Reviewer #3 (Recommendations For The Authors):
Line 81 - delete 's
Done.
Generally, the introduction was very well written and clearly summarised our current understanding but the paragraph beginning line 134 felt out of place and repeated some of the work mentioned earlier.
We have removed this paragraph.
For the EM analysis throughout quantification would be useful as highlighted in the public review. How many tomograms were examined, and how often were types of structures seen? I understand the sample size is often small but this would help the reader appreciate the diversity of structures seen.
We have included the numbers.
Following on from this how were the cells chosen for tomogram analysis? For example, the dividing cell in 1D has palisades associating with the new pocket - is this commonly seen? Does this reflect something happening in dividing cells. This point about endosomal division was picked up in the discussion but there was little about in the main results.
This issue is undoubtedly inherent to the method itself, and we have made efforts to mitigate it by generating a series of tomograms recorded randomly. We have refrained from delving deeper into the intricacies of the cell cycle in this manuscript, as we believe that it warrants a separate paper.
As the authors prosecute, the co-localisation analysis highlights the variable nature of the endosome and the overlap of different markers. When looking at the LM analysis, I was struck by the variability in the size and number of labelled structures in the different cells. For example, in 3A Rab7 is 2 blobs but in 3B Cell 1 it is 4/5 blobs. Is this just a reflection of the increase in the endosome during the cell cycle?
The variability in representation is a direct consequence of the dynamic nature of the labelled structures. For this reason, we deliberately selected different cells to represent examples of how the labelling can look like. We have decided not to mention the dynamics of the endosome during the cell cycle. This will be the subject of a further report.
Moreover, Rab 11 looks to be the marker covering the greatest volume of the endosomal system - is this true? I think there's more analysis of this data that could be done to try and get more information about the relative volumes etc of the different markers that haven't been drawn out. The focus here is on the co-localisation.
Precisely because we recognize the importance of this point, we intend to turn our attention to the cell cycle in a separate publication.
I appreciate that it is an awful lot of work to perform the immuno-EM and the data is of good quality but in the text, there could be a greater effort to tie this to the LM data. For example, from the Rab11 staining in LM you would expect this marker to be the most extensive across the networks - is this reflected in the EM?
For the immuno-EM there were no numbers, the authors had measured the position of the gold but what was the proportion of gold that was in/near membranes for each marker? This would help the reader understand both the number of particles seen and the enrichment of the different regions.
Our original intent was to perform a thorough quantification (using stereology) of the immuno-EM data. However, we later realized that the necessary random imaging approach is not suitable for Tokuyasu sections of trypanosomes. In short, the cells are too far apart, and the cell sections are only occasionally cut so that the endosomal membranes are sufficiently visible. Nevertheless, we continue to strive to generate more quantitative data using conventional immuno-EM.
The innovative combination of Tokuyasu tomograms with immuno-EM was great. I noted though that there was a lack of fenestration in these models. Does this reflect the angle of the model or the processing of these samples?
We are grateful to the referee, as we have asked ourselves the same question. However, we do not attribute the apparent lack of fenestration to the viewing angle, since we did not find fenestration in any of the Tokuyasu tomograms. Our suspicion is more directed towards a methodological problem. In the Tokuyasu workflow, all structures are mainly fixed with aldehydes. As a result, lipids are only effectively fixed through their association with membrane proteins. We suggest that the fenestration may not be visible because the corresponding lipids may have been lost due to incomplete fixation.
We now clearly state this in the lines 563 – 568.
“Interestingly, these tomograms did not exhibit the fenestration pattern identified in conventional electron tomography. We suspect that this is due to methodological reasons. The Tokuyasu procedure uses only aldehydes to fix all structures. Consequently, effective fixation of lipids occurs only through their association with membrane proteins. Thus, the lack of visible fenestration is likely due to possible loss of lipids during incomplete fixation.”
The discussion needs to be reworked. Throughout it contains references to results not in the main results section such as supplementary movie 2 (line 735). The explicit references to the data and figures felt odd and more suited to the results rather than the discussion. Currently, each result is discussed individually in turn and more effort needs to be made to integrate the results from this analysis here but also with previous work and the data from other organisms, which at the moment sits in a standalone section at the end of the discussion.
We have improved the discussion and removed the previous supplementary movies 2 and 3. Supplementary movie 1 is now mentioned in the results section.
Line 693 - There was an interesting point about dividing cells describing the maintenance of endosomes next to the old pocket. Does that mean there was no endosome by the new pocket and if so where is this data in the manuscript? This point relates back to my question about how cells were chosen for analysis - how many dividing cells were examined by tomography?
The fate of endosomes during the cell cycle is not the subject of this paper. In this manuscript we only show only one dividing cell using tomography. An in-depth analysis focusing on what happens during the cell cycle will be published separately.
Line 729 - I'm unclear how this represents a polarization of function in the flagellar pocket. The pocket I presume is included within the endosomal system for this analysis but there was no specific mention of it in the results and no marker of each position to help define any specialisation. From the results, I thought the focus was on endosomal co-localisation of the different markers. If the authors are thinking about specialisation of the pocket this paper from Mark Field shows there is evidence for the exocyst to be distributed over the entire surface of the pocket, which is relevant to the discussion here. Boehm, C.M. et al. (2017) The trypanosome exocyst: a conserved structure revealing a new role in endocytosis. PLoS Pathog. 13, e1006063
We have formulated our statement more cautiously. However, we are convinced that membrane exchange cannot physically work without functional polarization of the pocket. We know that Rab11, for example, is not evenly distributed on the pocket. By the way, in Boehm et al. (2017) the exocyst is not shown to cover the entire pocket (as shown in Supplementary Video 1).
We now refer to Boehm et al. (Lines 700 – 703):
“Boehm et al (2017) report that in the flagellar pocket endocytic and exocytic sites are in close proximity but do not overlap. We further suggest that the fusion of EXCs with the flagellar pocket membrane and clathrin-mediated endocytosis take place on different sites of the pocket. This disparity explains the lower colocalization between TbRab11 and TbRab5A.”
Line 735 - link to data not previously mentioned I think. When I looked at this data I couldn't find a key to explain what all the different colours related to.
We have removed the previous supplementary movies 2 and 3. We now reference supplementary movie 1 in the results section.
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www.gutenberg.org www.gutenberg.org
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Grappling with Grendel. To God I am thankful To be suffered to see thee safe from thy journey.
Annotation by: Samuel Godinho CC License: CC- BY-NC Tag: #SP2025-LIT211
I find the religious tension within the poem to be very interesting. The narrator and Beowulf frequently reference God and divine justice, but the poem still upholds Paganism and pagan ideals like fate and blood vengeance. This also shows the transitional period in which it was written, showing a cultural tug of war with the merging of old beliefs and emerging Christian values. The original poem shows many pagan values but once it was transcribed and translated it took on more Christian characteristics. This is an example of how religious values influenced this text.
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When my earth-joys were over, thou wouldst evermore serve me In stead of a father; my faithful thanemen, My trusty retainers, protect thou and care for, Fall I in battle: and, Hrothgar belovèd,
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Linguistic and Cultural Context: Hall’s translation is from the 1800s, so it uses older and fancier words to describe Beowulf and how his characteristics make him a hero. Gummere’s translation is from the early 1900s and is easier to read using more of modern texts and descriptions. These differences show how ideas of heroism and masculinity can change over time, even though Beowulf is always a strong, brave hero.
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Beowulf spake, Ecgtheow’s son: “Recall now, oh, famous kinsman of Healfdene, Prince very prudent, now to part I am ready, Gold-friend of earlmen, what erst we agreed on
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Comparative Insight: Both versions show Beowulf as a brave and respectful hero, but Hall’s version is more poetic, which makes Beowulf seem like a legendary figure. Gummere’s version is simpler and makes Beowulf seem more like a real person narrating the story. Both connect to gender politics by highlighting how a hero must be strong but also respectful.
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Beowulf spake, Ecgtheow’s son: “Recall now, oh, famous kinsman of Healfdene,
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Analysis: In this version, Beowulf is shown as a respectful hero where we can see here how he talks to the king to get approval before taking action. This shows male characteristics that are liked such as polite, honarable and being loyal. These connect to political gender as it emphasizes the qualities of traditional male characteristics.
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www.ontario.ca www.ontario.ca
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Renewal for children under 15 ½Submit your renewal application online
These two headings and generally all other headings on the page are using appropriate HTML tags to signify their semantic order and flow on the page. "Renewal for children under 15 and 1/2" is using an h2 tag while the sub-heading "Submit your renewal application online" is using an appropriate semantically correct h3 tag, which was found on inspection using dev tools. This allows screen readers to properly parse the page and also gives proper visual indication that one is a heading and the other is a sub-heading. This corresponds to the principle of "perceivable" because information is clearly being presented to users in a way they can perceive whether via the screen reader correctly parsing the text, or by visually with clear visual differences indicating the semantics and order of the content.
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Learn how to renew an Ontario health card. You need a valid card to get coverage through the Ontario Health Insurance Plan (OHIP).
(Reference to the image to the right of this text) The image of the Ontario Health Card on the top of the page has an alt attribute (inspected using dev tools) less than 125 characters that reads "Ontario health card" which is concise and describes the image. (Screen readers will detect it is an img tag and say something along the lines of "image of" and then read the alt attribute text). This corresponds to the web accesibility principle of "robust" as the descriptive and concise alt attribute allows the image to be interpreted by a wide variety of assistive technologies.
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www.myjewishlearning.com www.myjewishlearning.com
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Joseph’s life is a series of highs and lows — literally and figuratively. In his father’s house, Joseph is the favored son: “Israel (another name for Jacob) loved Joseph more than all his sons since he was a child of his old age” (Genesis 37:3). Joseph likely also has this status because he is the eldest child of Jacob’s favorite (deceased) wife, Rachel. To demonstrate this preference, Jacob gifts Joseph with the famous kitonet passim, translated as both a garment with long sleeves, or a fine woolen tunic. (Commentators extrapolate that it had stripes of different colors.) This preferential treatment from their father elicits much jealousy from Joseph’s 10 older brothers.
Annotation about josey's favoritism towards him by his father. Author: David Sanchez CC License: CC BY-NC Tag: #SP2025-Lit211
The story of Joseph in the book of Genesis shows us some of the aspects that marked the present and future of his life. The book of Genesis tells us about the favoritism and devotion that his father Jacob always had towards him, being the favorite son of 12 brothers. “Israel (another name for Jacob) loved Joseph more than all his sons since he was a child of his old age” (Genesis 37:3). This favoritism towards Joseph on the part of Jacob was because Joseph was the firstborn of the woman that Jacob had loved the most, who was Rachel. As a sign of his love and affection, Jacob gave him a colorful tonic (ketones passim), which symbolized a gesture of favoritism towards Joseph and aroused the anger and fury of his brothers. These texts show us how favoritism towards certain members of a family is something bad and unnecessary, even for the beneficiary who in this case was Joseph, because this blatant favoritism on the part of Jacob was what somehow caused Joseph to be sold by his brothers to the Ishmaelites, thus causing a very tragic situation for Jacob's family.
References: The Holy Bible: New Revised Standard Version. Genesis 37:3.
Roth, Elana. “The Story of Joseph.” My Jewish Learning, 20 June 2023, www.myjewishlearning.com/article/the-story-of-joseph/.
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Joseph’s life is a series of highs and lows — literally and figuratively. In his father’s house, Joseph is the favored son: “Israel (another name for Jacob) loved Joseph more than all his sons since he was a child of his old age” (Genesis 37:3). Joseph likely also has this status because he is the eldest child of Jacob’s favorite (deceased) wife, Rachel. To demonstrate this preference, Jacob gifts Joseph with the famous kitonet passim, translated as both a garment with long sleeves, or a fine woolen tunic. (Commentators extrapolate that it had stripes of different colors.) This preferential treatment from their father elicits much jealousy from Joseph’s 10 older brothers.
Annotation about josey's favoritism towards him by his father. Author: David Sanchez CC License: CC BY-NC Tag: #SP2025-Lit211
The story of Joseph in the book of Genesis shows us some of the aspects that marked the present and future of his life. The book of Genesis tells us about the favoritism and devotion that his father Jacob always had towards him, being the favorite son of 12 brothers. “Israel (another name for Jacob) loved Joseph more than all his sons since he was a child of his old age” (Genesis 37:3). This favoritism towards Joseph on the part of Jacob was because Joseph was the firstborn of the woman that Jacob had loved the most, who was Rachel. As a sign of his love and affection, Jacob gave him a colorful tonic (ketones passim), which symbolized a gesture of favoritism towards Joseph and aroused the anger and fury of his brothers. These texts show us how favoritism towards certain members of a family is something bad and unnecessary, even for the beneficiary who in this case was Joseph, because this blatant favoritism on the part of Jacob was what somehow caused Joseph to be sold by his brothers to the Ishmaelites, thus causing a very tragic situation for Jacob's family.
References: The Holy Bible: New Revised Standard Version. Genesis 37:3.
Roth, Elana. “The Story of Joseph.” My Jewish Learning, 20 June 2023, www.myjewishlearning.com/article/the-story-of-joseph/.
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upoitiers86-my.sharepoint.com upoitiers86-my.sharepoint.com
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che s’inscrit dans le
test 2
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www.nasa.gov www.nasa.gov
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You may have come across the tag "BURNBABY" in connection with the LM powered flight software. That was us. We might not have been out on the streets, but we did listen to the news, and the two biggest news stories were Viet Nam and Black Power, the latter including H. Rap Brown and his exhortations to 'Burn Baby, Burn' -- this was 1967, after all.
Not the Magnificent Montgue
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www.biorxiv.org www.biorxiv.org
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Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.
Learn more at Review Commons
Reply to the reviewers
Manuscript number: RC-2025-02887
Corresponding author(s): Philippe Bastin
1. General Statements [optional]
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We thank the reviewers for their constructive suggestions. We are delighted to see that they appreciated our work and its interest for the broad cell biology community, as well as the potential impact of the inducible expression of tagged tubulin as a new tool to investigate microtubule assembly at large.
We are now providing a full revision that contains two major modifications and that addresses all the minor points detailed below. The two major modifications are:
- A simplification and a shortening of the text as requested by reviewers 1 and 3
- The addition of a new experiment evaluating the role of the locking protein CEP164C to gain insight into the mechanism, as suggested by reviewers 1 and 2 Briefly, CEP164C is a protein localised to the transition fibres (structures that dock the basal body of the flagellum to the membrane) of only the old flagellum. Its depletion leads to an excessive elongation of the old flagellum and the production of a shorter new flagellum, suggesting competition between the two flagella for tubulin incorporation (Atkins et al., 2021). In the new figure 5, we have expressed tagged tubulin in the CEP164CRNAi cell line and formally demonstrated simultaneous incorporation in both flagella. Unexpectedly, the new flagellum incorporated more tubulin than the old one, suggesting a bias of tubulin targeting in favour of the new flagellum and the existence of additional contributors to the Grow-and-Lock model.
2. Point-by-point description of the revisions
This section is mandatory. *Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. *
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Reviewer #1
Evidence, reproducibility and clarity
The manuscript by Daniel Abbühl on "A novel approach to tagging tubulin reveals MT assembly dynamics of the axoneme in Trypanosoma brucei" uses an innnovative approach to label tubulin, which allows the authors to unveil new mechanisms in flagellar length regulation.
The manuscript is very nice and will be very interesting for the cell biology community and therefore should be accepted. In some parts it becames a bit complex with all the models and complex phrasing, I wonder whether the text could be simplified to be more appealing. I have a few minor comments:
We agree that some of the explanations are lengthy and complex. We have simplified the explanations and hopefully made the models more accessible. Complexity comes from the fact that trypanosomes do not have a synchronized cell cycle.
-From the model the authors show in Figure 8- there should be a way of pulsing the cells in G1 for a short amount of time -2 hours- and getting both flagella tips labelled. But the authors seem to require longer labelling to get that result. This should be better explained.
We are not quite sure what is meant here with both flagella as in G1-phase, all cells are mono-flagellated. We do see mono-flagellated cells with a labelled tip after 2 hours, both with the HALO-tag or the Ty-1-tubulin system.
In regard to bi-flagellate cells, we believe that incorporation in the OF happened at the beginning of G1-phase when the cell was mono-flagellated. If tubulin is present at that point, it will be incorporated at the tip. This cell then approaches the end of G1-phase and starts to initiate NF assembly. Since tagged tubulin is already present it will be incorporated along the whole length of the NF.
A short induction of 2h would not suffice as it wouldn't cover the duration of the G1-phase and the initiation of a NF (duration of G1-phase is ~4h). We attempted to explain this in Fig. 4 and reworked the text to make this clearer.
-Why do some cells not express the construct? Weren´t they all selected?
We never managed to get a cell line where inducible expression is present in 100% of cells. Here, around 95% of cells were positive for Ty-1-tubulin after 24h of induction. Non-expression is not a phenomenon restricted to this tubulin cell line but also observed with other ectopically expressed proteins (e.g. Sunter et al. JCS 2015, Bastin et al. MCB 1999). All these cell lines represent clonal populations and are resistant to antibiotic treatment, however not all cells express the respective protein. For each experiment where we believed the number of expressing cells matter (for example the washout), we quantified in how many cells Ty-1-tubulin was present in the cell body microtubules.
-"The linear regression line in Fig. 3C was corrected by subtracting 45 minutes from each timepoint due to the previously reported delay between addition of tetracycline and the expression of the respective protein". However, in the authors data the delay may amount to one hour (western analysis- S4). Shouldn´t they use their data.
Indeed, the western blot shows expression after 1-hour, however we did not take a 45-minute timepoint, so we don't know if the protein was detectable at that time. In addition, IFA is more sensitive than western blot. We cannot say exactly when the average cell starts to express the induced protein.
-Fig 3: To measure the timepoints of flagella growth, wouldn´t it be better to do it with NF that started to grow before induction, rather than starting to grow after induction, to be sure that the timing of incorporation is fully accounted for?
We indeed did consider only NFs, which started to grow before induction, as suggested by the reviewer. In the revised version the description of the experiment can be found on page 9 line 22 - 28.
-Although it is not the focus of the manuscript it would have been very interesting to use the CEP164C mutant to see whether it would change the dynamics of incorporation and fully test their model and discussion.
This is a great suggestion, so we performed some experiments to address this issue. When CEP164C was knocked down before Ty-1-tubulin expression, integration is seen at the distal tip of both NF and OF. This is coherent with the idea of removal of the locking protein from the OF. However, lengths of the green segments in NF and OF do not have the same length (NF ~6 µm, OF ~2 µm), which indicates that CEP164C might not be the only protein involved in regulating flagellum length. A new figure explaining this experiment was added (Fig. 5, Fig. S6). We believe this data provides novel insight on the locking mechanism and strengthens the manuscript.
-In some parts of the manuscript/supplemental material the authors say they insert the Ty-1- tag one aminoacid after the acetylated lysine- other parts they say two aminoacids after- this should be consistent.
We thank the reviewer for spotting these mistakes, we have changed the text accordingly.
-Fig. S1: 'Binding epitope of the TAT-1 antibody is highlighted in red'. There is no highlighting in red in this figure?
This sentence was removed.
-Fig. S2: Western blots are not very clear. What is the 'X' present in the C (first lane)? Weight of markers should be shown also in S4.
Molecular weight markers have been added. X is an empty lane, we have now indicated this in the figure legend.
-Fig 5: 'C: Frequency of bi-flagellated cells grouped by the different types of' The authors didn't finish the sentence.
Previous Fig. 5 is now Fig. 6. Sentence has been completed. "Frequency of bi-flagellated cells grouped by different types of old flagella"
-Fig. S7: The 'B' is missing in both picture and legend.
This has been added
Significance
This study advances our knowledge of flagellar length regulation and maintenance. Moreover, the tools designed in this work will be very useful for the cell biology community in general.
Reviewer #2
Evidence, reproducibility and clarity
Summary: The length of the old flagellum of Trypanosome is constant during G1 phase as well as during cell cycle progression when the new flagellum is assembled. The authors have previously proposed a "Grow and Lock" model for the flagellar length control in which no flagellar building blocks are incorporated. To test this hypothesis, the authors used a tagging strategy for alpha-tubulin and tracking its incorporation. The authors showed that the new flagellum incorporates new tubulins, as is expected. For the mature flagellum, tubulins are incorporated at the flagellar tip and only when the cells start to assemble the new flagellum. Thus, it shows that old flagellum is stable but not completely locked for the incorporation of tubulins.
Major comments: The study is methodologically rigorous, integrating fluorescence microscopy, biochemical approaches, and proteomic analyses to validate the functionality of the tagged tubulin. The use of both inducible expression and endogenous protein tagging (HaloTag) strengthens the conclusions. This study has supported the "Grow-and-Lock" model" that the authors previously proposed. In addition, they have revealed that the stability of the old flagellum is temporally controlled.
The data showed that brief incorporation of tubulins at the tip of the old flagellum occurs when the cells start to form the new flagellum. I thought the assembly of the new flagellum occurs during the cell division. However, in the abstract, it says that "The restriction is lifted briefly after the bi-flagellated cell has divided." Is my understanding wrong?
We believe incorporation at the tip of the "OF" occurred after the cell has divided, when the OF daughter is mono-flagellated. It happens before this daughter cells starts assembling its new flagellum is formed. Of course, when looking at biflagellated cells, the NF as well as the tip of the OF will be green, but our data supports that incorporation happened in G1-phase and not during the biflagellated stage as the lock seals the OF before the NF emerges. To clarify on terminology: The bi-flagellate stage begins when basal bodies are duplicated, shortly after the beginning of S-phase and ends with cytokinesis. This means G1-phase and the mono-flagellated stage are nearly the same (Woodward and Gull, JCS1990) and occupy ~40% of the cell cycle.
P12, "The cartoon in Fig. 5A illustrates the progression of the cells in scenario 2 (Fig. 4A) over the duration of one cell cycle (~9 hours)" I thought that one cell cycle should start with cell with only one flagellum, followed by assembly of a new flagellum during cell division, the cell then divides when the new flagellum is almost completely assembled. If my understanding is correct, perhaps the cartoon should be modified accordingly.
Indeed, the cell cycle starts with a cell in G1-phase. Here, we have chosen the initiation of a NF assembly as our starting point because we focused the investigation on bi-flagellated cells. We have now illustrated the cell cycle (adapted from Woodward and Gull 1990) and when cells are biflagellated in Fig. 6A (revised version).
Minor comments:
1) Several references are not correctly formatted. P3: (Flavin and Slaughter, 1974) (Rosenbaum 1969). P10, (Sherwin et al., 1987)(Sheriff et al., 2014) 2) In several places there are no space between the number and the unit. For eample, P3, 9 - 24µm/h. 7, 1μg/m; P8, 50kDa; P9, 1M; 8-9h; P11, 2.9µm/h and etc. 3) P11, Flagella were extracted. I thought the cells were extracted.
Thank you for pointing these out, we have changed these in the text.
Significance
Cilia and eukaryotic flagella are considered dynamic structures in which the flagellar components especially tubulins under constant turnovers even in steady state. This work demonstrates that in Trypanosome the stable old flagellum is temporally controlled for tubulin turnovers, suggesting a tight regulation of microtubule dynamics. Future elucidation of the regulatory mechanism will be more interesting. This work will be interesting to the field of cilia and microtubules. In addition, the new technique used for tracking tubulins will also be interesting.
I am an expert on ciliary biology.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
Summary:
This study seeks to investigate the mechanism by which the length of an eukaryotic cilium is set and maintained in a constant state. The flagellated protist Trypanosoma brucei serves as the study model and the authors take advantage of the genetic tools that allow precise modification and tagging of flagellar proteins and they build on prior knowledge about the well-characterised flagellar assembly cycle, which allows tracking the assembly of a new flagellum alongside an existing old one in the course of one cell cycle. The group of Bastin has previously reported a very interesting "Grow-and-Lock Model for the Control of Flagellum Length in Trypanosomes" and this current manuscript provides a test of this model, and a refinement. Key to this is an advance in technique, reported here, namely expression of an epitope tagged version of alpha tubulin. The epitope is inserted in an internal loop, which apparently for the first time provides a traceable tubulin that is reliably incorporated into the cytoskeleton (subpellicular array, spindle and cilium). Expressing an inducible version of this Ty-1-tubulin allows for a set of experiments that measure the place and timing of tubulin incorporation into cilia. The results are largely confirmatory of previous findings (incorporation exclusively into the new flagellum, at the distal end, linear growth rate that matches previous estimates). Examination of tubulin incorporation patterns then reveal additional information about the old flagellum: evidence from Ty-1-tubulin labelling, corroborated by incorporation patterns of another ciliary protein (RSP 4/6) suggest that the "lock" on the old flagellum is relieved for short periods after cell division, leading to a refined model presented in Figure 8.
Major comments:
This study provides an elegant test of the grow-and-lock model and the major conclusions are supported by the data. I have no major concerns.
Minor comments:
There are several minor points that could be addressed to make the manuscript easier to follow (and adding line numbers to the manuscript would help with reviewing).
The introduction is quite long. Some of the well-established background information on the T. brucei cell cycle could be shortened. If the paper is intended for a broader audience, it would be valuable instead to cite studies that have succeeded in tagging tubulin and tracing its incorporation in other cilia. Could the Ty-1-tubulin approach be relevant more broadly or are simpler methods already established?
The introduction has been shortened, we now also cite two published studies that tracked tubulin integration in Chlamydomonas and C. elegans respectively.
On p.6 the rationale for endogenous tagging was to "reduce the risk of artifacts portentially due to untimely expression or unnatural protein levels". However most of the experiments were done with ectopically expressed inducible Ty-1-tubulin. For the experiments it is crucial to use an inducible system but the authors may wish to comment why the risk of artifacts was no longer a concern.
The reasoning here was that in case the Ty-1-tubulin would not have been incorporated into MTs, we could have attributed it solely to the presence of the tag and no other factors, but this was not the case. This therefore allowed us to move to the inducible expression system.
On p.7 / Fig S2A-B there appears to be a mistake in the presentation. Spindles are mentioned in the text - I can't see any in the figure. Fig S2A and B both show cytoskeletons, but the text suggests only B is about cytoskeletons. None of the blot shows BB2 staining of different cell fractions, contrary to statements in the text. The letter codes in the panel (T, C, D) don't match the codes in the legend (T, P, S).
We thank the reviewer for spotting the mistakes. A panel with the spindle was added in Fig. S2. We did not stain fraction blots of the in-situ tagged cell lines with BB2. However, this was done with the inducible cell line and is shown in Fig. 1D. Letter code in the legend was adapted to match the figure.
Figure 1. The evidence for incorporation into spindles is not strong. The structure indicated by the arrive could be a spindle but it's not very clear. There is a great example of a labelled spindle only in figure S5A. Here, at the start, it would be good to show a panel of cells in successive cell cycle stages (best, whole cells and cytoskeletons) to clearly show the structures that are labelled with Ty-1-tubulin.
The current Fig. 1B (Fig. 1A before) depicts whole cells of an induced and a non-induced culture; we show whole cells to provide a complete picture of tubulin integration. A panel with detergent extracted cytoskeletons from the in situ tagged cell line has been added to Fig. 1A. We chose to show cytoskeletons or isolated flagella instead of whole cells because (1) the flagella are easier to see and (2) it formally demonstrates that tagged tubulin is incorporated in MTs.
In general, tubulin labelling of the spindle was more consistently observed in whole cells as we did not use spindle preserving extraction buffers when preparing cytoskeletons. However, we did observe clear spindles in cytoskeletons as well (see Fig. S5 for example). The same was observed for the beta-tubulin specific KMX1 antibody in the past which is the gold standard to visualize the spindle (Sasse and Gull JCS1988). Regardless, a panel depicting spindle progression through mitosis using staining of Ty-1-tubulin has been added in Fig. S2 (The panel is a mix of whole cells and cytoskeletons).
On p.8 (end of first paragraph) there is reference to cell cycle analyses, but no data is shown. Also on p.8, please clarify what the evidence is that "a fraction of cells did not respond to tetracycline". The fact that they remain unstained by Ty-1-tubulin is not in itself evidence they did not respond to tetracycline.
We did not show the cell cycle data as it was similar to non-induced and does not provide any new information in our opinion. Hence, the sentence has been removed.
The reviewer is correct that we do not have evidence that these cells did not respond to tetracycline. Some cells remained completely devoid of Ty-1-tubulin even after multiple days of induction. This was typically between 5-10% of cells. In experiments where the exact number is important, we counted the amount of "non-expressers" in whole cells.
Figure S4A. The blot for the soluble fraction is not of great quality. I don't see how the conclusion was reached that the Ty-1-tubulin bands were faint.
The blot of the soluble fraction that was stained with BB2 had to be exposed a lot longer compared to the blot stained with TAT-1. The soluble blots were repeated with the same result (lots of background noise when using BB2, a clear blot with TAT-1). In the TAT-1 blot only the endogenous tubulin band is clearly visible, with some very faint signal above corresponding to the Ty-1-tubulin. Soluble Ty-1-tubulin with BB2 or TAT-1 is visible in Fig. 1D after longer inductions.
On p.11, it would be interesting to compare measured elongation rates with previously measured estimates for flagellum growth, comparing the growth rates, and relating them to cell cycle times in the corresponding experiments (which vary slightly between labs and studies).
We attempted to address this in the discussion by comparing our experiments to the assembly rate measured with the PFR as reporter (Bastin et al. 1999). We could mention the corresponding doubling times in correlation to how many cells are bi-flagellated, but this was only done with the Ty-1-tubulin cell line and not with the PFR. In our experiments the average doubling time was ~9 hours with 52% of cells being bi-flagellated. This was measured with FTZC (marker of the transition zone at the base of the flagellum) and Mab25 (marker of the axoneme of the flagellum) which will lead to a slight underestimate of the real number of bi-flagellated cells, as the NF is initially very close which makes it difficult to notice/differentiate from the old one.
Figure S6. I find the presentation of this figure confusing. It should be revised with clearer labelling of "cell cycle 1", "cell cycle 2", and the precise meaning of "type 3" should be clarified. There are two instances of "type 1" in the drawing, but one of these seems to fulfil the criteria of "type 3" (OF 1-4µm).
We agree with the reviewer and therefore decided to remove this figure. We also considered the comments of the other two reviewers about complexity of the manuscript and changed the text of figure 5 to make it more approachable. This includes a simpler explanation for the expected amounts of flagella.
Figure 7. In panel A, the absence of label at the NF distal end is not total, a purple line is still visible. Was any quantitation attempted (signal intensity, changes in length of labelled fragments over time?). Minimally, say how many cells were analysed for the numbers in panels D and E, and how many times this experiment was done.
We agree with the reviewer that the decrease in the TMR signal in the NF of the cell in the original Fig. 7A (currently Fig. 8A) is gradual and not abrupt. Similarly to the Ty-1-tubulin experiments where the tagged protein becomes progressively more available (increasing intensity), the intensity of TMR-ligand becomes progressively less abundant (gradually decreasing intensity) as new (not TMR labelled) protein gets synthesized during the period of NF construction, progressively diluting the initially fully labeled population of RSP4/6. The slope of the gradient may differ between axonemal constituents, as it reflects the kinetics of protein synthesis, degradation, its incorporation into the axoneme, as well as the size of the soluble protein pool in the cytosol. We classify this type of signal as gradients, as opposed to the sharp decrease. At initial times after TMR-ligand washout (e.g. 4 hours in Fig. 8C), this long gradient is observed at the distal end of NFs and in some uniflagellated cells (NF-inheriting daughters). The distal ends of OFs in these experiments (if not fully labelled) display a sharp decrease, as do frequent uniflagellated cells, likely OF-inheriting daughters. The existence of these two different patterns demonstrates that two different mechanisms are responsible for incorporation of fresh RSP4/6 into the NF and OF axoneme, respectively. While incorporation into the NF is gradual, incorporation into the distal region of the OF is stepwise (restricted in time). Numbers of cells quantified for the table in Fig. 8 have been added. The NFs and OFs displaying the patterns of the gradient and sharp decrease, respectively, were observed in multiple experiments.
Reviewer #3 (Significance (Required)):
- General assessment: strengths and limitations
Strengths: Trypanosoma brucei is a powerful model system in which to ask detailed questions about the assembly dynamics and hierarchy of microtubule-based cytoskeletal structures in general and cilia in particular. This elegant and well-designed study overcomes a previous technical limitation by allowing for the direct labelling of alpha tubulin, one of the main building blocks of the ciliary axoneme. The study sets out to test a specific hypothesis (grow-and-lock model) and provides evidence in support, leading to a refined model for cilia length regulation in trypanosomes.
Limitations: With this system, visualisation of new tubulin incorporation requires de novo synthesis. There is a time lag between inducing expression of Ty-1-tubulin with tetracycline and being able to visualize the tagged proteins that needs to be taken into consideration. This time lag was estimated based on previous studies and the relatively quick appearance of Ty-1-tubulin on Western blots (within hours). This inevitably creates a situation where levels of tagged tubulin change rapidly, creating gradients of signal intensity (and variations in levels) that lead to some uncertainty in estimations of length of labelled microtubule fragments. Furhtermore, the epitope label is not compatible with live cell imaging, restricting analyses to fixed cells. The Ty-1-tubulin data is well ducmented; the RSP4/6 data appear to corroborate these findings but are less extensively documented.
- Advance: The results succeed in integrating several recent findings from different research groups into a refined coherent model about cilia length regulation in trypanosomes. The tubulin tagging method could be gainfully transferred to other systems (although the state of the field in tubulin tagging in other systems is not clearly laid out in the paper).
This paper could be of interest to a broad cell biology community interested in cilia and cytoskeletal dynamics.
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Referee #1
Evidence, reproducibility and clarity
The manuscript by Daniel Abbühl on "A novel approach to tagging tubulin reveals MT assembly dynamics of the axoneme in Trypanosoma brucei" uses an innnovative approach to label tubulin, which allows the authors to unveil new mechanisms in flagellar length regulation.
The manuscript is very nice and will be very interesting for the cell biology community and therefore should be accepted. In some parts it becames a bit complex with all the models and complex phrasing, I wonder whether the text could be simplified to be more appealing. I have a few minor comments:
- From the model the authors show in Figure 8- there should be a way of pulsing the cells in G1 for a short amount of time -2 hours- and getting both flagella tips labelled. But the authors seem to require longer labelling to get that result. This should be better explained.
- Why do some cells not express the construct? Weren´t they all selected?
- "The linear regression line in Fig. 3C was corrected by subtracting 45 minutes from each timepoint due to the previously reported delay between addition of tetracycline and the expression of the respective protein". However, in the authors data the delay may amount to one hour (western analysis- S4). Shouldn´t they use their data.
- Fig 3: To measure the timepoints of flagella growth, wouldn´t it be better to do it with NF that started to grow before induction, rather than starting to grow after induction, to be sure that the timing of incorporation is fully accounted for?
- Although it is not the focus of the manuscript it would have been very interesting to use the CEP164C mutant to see whether it would change the dynamics of incorporation and fully test their model and discussion.
- In some parts of the manuscript/supplemental material the authors say they insert the Ty-1- tag one aminoacid after the acetylated lysine- other parts they say two aminoacids after- this should be consistent.
- Fig. S1: 'Binding epitope of the TAT-1 antibody is highlighted in red'. There is no highlighting in red in this figure?
- Fig. S2: Western blots are not very clear. What is the 'X' present in the C (first lane)? Weight of markers should be shown also in S4.
- Fig 5: 'C: Frequency of bi-flagellated cells grouped by the different types of' The authors didn't finish the sentence.
- Fig. S7: The 'B' is missing in both picture and legend.
Significance
This study advances our knowledge of flagellar length regulation and maintenance. Moreover the tools designed in this work will be very useful for the cell biology community in general.
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www.biorxiv.org www.biorxiv.org
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Author response:
The following is the authors’ response to the original reviews
Public Reviews:
Reviewer #1 (Public review):
Summary:
This study focuses on characterizing a previously identified gene, encoding the secreted protein Ppe1, that may play a role in rice infection by the blast fungus Magnaporthe oryzae. Magnaporthe oryzae is a hemibiotrophic fungus that infects living host cells before causing disease. Infection begins with the development of a specialized infection cell, the appressorium, on the host leaf surface. The appressorium generates enormous internal turgor that acts on a thin penetration peg at the appressorial base, forcing it through the leaf cuticle. Once through this barrier, the peg elaborates into bulbous invasive hyphae that colonizes the first infected cell before moving to neighboring cells via plasmodesmata. During this initial biotrophic growth stage, invasive hyphae invaginate the host plasma membrane, which surrounds growing hyphae as the extra-invasive hyphae membrane (EIHM). To avoid detection, the fungus secretes apoplastic effectors into the EIHM matrix via the conventional ER-Golgi secretion pathway. The fungus also forms a plant-derived structure called the biotrophic interfacial complex (BIC) that receives cytoplasmic effectors through an unconventional secretion route before they are delivered into the host cell. Together, these secreted effector proteins act to evade or suppress host innate immune responses. Here the authors contribute to our understanding of M. oryzae infection biology by showing how Ppe1, which localizes to both the appressorial penetration peg and to the appressorial-like transpressoria associated with invasive hyphal movements into adjacent cells, maximizes host cell penetration and disease development and is thus a novel contributor to rice blast disease.
We sincerely appreciate the reviewer’s thoughtful evaluation of our work. We are grateful for your recognition of Ppe1 as a novel contributor to M. oryzae infection biology and your insightful summary of its spatio-temporal localization and functional importance in host penetration. We also appreciate devoting your time to provide us with constructive feedback, which greatly strengthens our manuscript.
Strengths:
A major goal of M. oryzae research is to understand how the fungus causes disease, either by determining the physiological underpinnings of the fungal infection cycle or by identifying effectors and their host targets. Such new knowledge may point the way to novel mitigation strategies. Here, the authors make an interesting discovery that bridges both fungal physiology and effector biology research by showing how a secreted protein Ppe1, initially considered an effector with potential host targets, associates with its own penetration peg (and transpressoria) to facilitate host invasion. In a previous study, the authors had identified a small family of small secreted proteins that may function as effectors. Here they suggest Ppe1 (and, later in the manuscript, Ppe2/3/5) localizes outside the penetration peg when appressoria develops on surfaces that permit penetration, but not on artificial hard surfaces that prevent peg penetration. Deleting the PPE1 gene reduced (although did not abolish) penetration, and a fraction of those that penetrated developed invasive hyphae that were reduced in growth compared to WT. Using fluorescent markers, the authors show that Ppe1 forms a ring underneath appressoria, likely where the peg emerges, which remained after invasive hyphae had developed. The ring structure is smaller than the width of the appressorium and also lies within the septin ring known to form during peg development. This so-called penetration ring also formed at the transpressorial penetration point as invasive hyphae moved to adjacent cells. This structure is novel, and required for optimum penetration during infection. Furthermore, Ppe1, which carries a functional signal peptide, may form on the periphery of the peg, together suggesting it is secreted and associated with the peg to facilitate penetration. Staining with aniline blue also suggests Ppe1 is outside the peg. Together, the strength of the work lies in identifying a novel appressorial penetration ring structure required for full virulence.
We are deeply grateful to the reviewer for the clear understanding and insightful evaluation of our work. Your recognition of the novel contribution and scientific merit of our study is both encouraging and motivating. We sincerely appreciate the time, expertise and constructive feedback dedicated to reviewing our manuscript, as the comments have been instrumental in enhancing the quality of this work.
Weaknesses:
The main weakness of the paper is that, although Ppe1 is associated with the peg and optimizes penetration, the function of Ppe1 is not known. The work starts off considering Ppe1 a secreted effector, then a facilitator of penetration by associating with the peg, but what role it plays here is only often speculated about. For example, the authors consider at various times that it may have a structural role, a signaling role orchestrating invasive hyphae development, or a tethering role between the peg and the invaginated host plasma membrane (called throughout the host cytoplasmic membrane, a novel term that is not explained). However, more effort should be expended to determine which of these alternative roles is the most likely. Otherwise, as it stands, the paper describes an interesting phenomenon (the appressorial ring) but provides no understanding of its function.
We sincerely appreciate the reviewer’s comments. We have revised "host cytoplasmic membrane" to "host plasma membrane" throughout the manuscript for consistency. To further investigate the role of the Ppe1 in the interaction between M. oryzae and rice, we overexpressed PPE1 in rice ZH11. A pCXUN-SP-GFP-Ppe1 vector containing a signal peptide and an N-terminal GFP tag was constructed (pCXUN-SP-GFP-Ppe1), and 35 GFP-PPE1-OX plants (T0) were subsequently obtained through Agrobacterium-mediated rice transformation. Subsequently, PCR and qRT-PCR validation were performed on the T0 transgenic plants. The PCR results showed that the inserted plasmid could be amplified from the genomic DNA extracted from the leaves of all the resulting T0 plants (Author response image 1A). qRT-PCR results indicated that most T0 transgenic plants could transcriptionally express PPE1 (Author response image 1B). T0 plants with higher expression levels were selected for western blot analysis, which confirmed the presence of GFP-Ppe1 bands of the expected size (Author response image 1C). To further explore the targets of Ppe1 in rice, the leaf sheaths of T0 plants were inoculated with M. oryzae strain Guy11. Total proteins were extracted at 24 hours post-inoculation (hpi) and subjected to immunoprecipitation using GFP magnetic beads. Silver staining revealed more interacting protein bands in T0 plants compared to ZH11 and GFP-OX controls (Author response image 1D). These samples were then analyzed by mass spectrometry in which 331 rice proteins that potentially interact with Ppe1 were identified (Author response image 1E). Subsequently, yeast two-hybrid assays were performed on 13 putative interacting proteins with higher coverage, but no interaction was detected between Ppe1 and these proteins (Author response image 1F-G). Considering that the identification and functional validation of interacting proteins is a labor-intensive and time-consuming endeavor, we will focus our future efforts on in-depth studies of Ppe1's function in rice.
Author response image 1.
Screening of Ppe1 candidate targets in rice. (A) The determination of GFP-PPE1 construct in transgenic rice. (B) The expression of PPE1 transgenic rice (T0) was verified by qRT-PCR. (C) Western blot analysis of Ppe1 expression in transgenic rice. (D) Rapid silver staining for detection of the purified proteins captured by the GFP-beads. (E) Venn diagram comparing the number of proteins captured in the different samples. (F) Identity of the potential targets of Ppe1 in rice. (G) Yeast two-hybrid assay showing negative interaction of Ppe1 with rice candidate proteins.
The inability to nail down the function of Ppe1 likely stems from two underlying assumptions with weak support. Firstly, the authors assume that Ppe1 is secreted and associated with the peg to form a penetration ring between the plant cell wall and cytoplasm membrane. However, the authors do not demonstrate it is secreted (for instance by blocking Ppe1 secretion and its association with the peg using brefeldin A).
To investigate the secretion pathway of Ppe1 in M. oryzae, we determined the inhibitory effects of Brefeldin A (BFA) on conventional ER-to-Golgi secretion in fungi as suggested by the reviewer. We inoculated rice leaf sheaths with conidia suspensions from the Ppe1-mCherry and PBV591 strains (containing a Pwl2-mCherry-NLS and Bas4-GFP co-expressing constructs) and treated them with BFA. We found that, even after exposure to BFA for 5 to 11 hours, the Ppe1-mCherry still formed its characteristic ring conformation (Author response image 2). Similarly, in the BFA-treated samples, the cytoplasmic effector Pwl2-mCherry accumulated at the BIC, while the apoplastic effector Bas4-GFP was retained in the invasive hyphae (Author response image 2). These results indicate that Ppe1 is not secreted through the conventional ER-Golgi secretion pathway.
Author response image 2.
The secretion of Ppe1 is not affected by BFA treatment. (A) and (B) The Ppe1-mCherry fluorescent signal was still observed both in the presence and absence of BFA. (C) Following BFA treatment, the secretion of the apoplastic effector Bas4-GFP was blocked while that of the cytoplasmic effector Pwl2-mCherry was not affected. The rice leaf sheath tissue was inoculated with 50 μg/mL BFA (0.1% DMSO) at 17 hpi. Images were captured at 22 hpi for A and 28 hpi for B and C. Scale bars = 10 µm.
Also, they do not sufficiently show that Ppe1 localizes on the periphery of the peg. This is because confocal microscopy is not powerful enough to see the peg. The association they are seeing (for example in Figure 4) shows localization to the bottom of the appressorium and around the primary hyphae, but the peg cannot be seen. Here, the authors will need to use SEM, perhaps in conjunction with gold labeling of Ppe1, to show it is associating with the peg and, indeed, is external to the peg (rather than internal, as a structural role in peg rigidity might predict). It would also be interesting to repeat the microscopy in Figure 4C but at much earlier time points, just as the peg is penetrating but before invasive hyphae have developed - Where is Ppe1 then? Finally, the authors speculate, but do not show, that Ppe1 anchors penetration pegs on the plant cytoplasm membrane. Doing so may require FM4-64 staining, as used in Figure 2 of Kankanala et al, 2007 (DOI: 10.1105/tpc.106.046300), to show connections between Ppe1 and host membranes. Note that the authors also do not show that the penetration ring is a platform for effector delivery, as speculated in the Discussion.
We sincerely appreciate the reviewer's valuable suggestion regarding SEM with immunogold labeling to precisely visualize Ppe1's association with penetration peg. While we fully acknowledge this would be an excellent approach, after consulting several experts in the field, we realized that the specialized equipment and technical expertise required for fungal immunogold-SEM are currently unavailable to us. We sincerely hope that the reviewer will understand this technical limitation.
To further strengthen our evidence for the role of Ppe1's in anchoring penetration peg to the plant plasma membrane, we provided new co-localization images of Ppe1 and penetration peg (Fig. S7). At 16 hours post-inoculation (hpi), when the penetration peg was just forming and prior to the development of invasive hyphae, the Ppe1-mCherry fluorescence forms a tight ring-like structure closely associated with the base of the appressorium. As at 23 hpi, the circular Ppe1-mCherry signal was still detectable beneath the appressorium, and around the penetration peg which differentiated into the primary invasive hyphae. Furthermore, we obtained 3D images of the strain expressing both Ppe1-mCherry and Lifeact-GFP during primary invasive hyphal development. The results revealed that Ppe1 forms a ring-like structure that remains anchored to the penetration peg during fungal invasion (Fig. S6).
We also conducted FM4-64 staining experiment as recommended by the reviewer. Although the experiment provided valuable insights, we found that the resolution was insufficient to precisely delineate the spatial relationship between Ppe1 and host membranes at the penetration peg (Author response image 3). To optimize this colocalization, we tested the localization between Ppe1-mCherry ring and rice plasma membrane marker GFP-OsPIP2 (Fig. S8). These new results provide compelling complementary evidence supporting our conclusion that Ppe1 functions extracellularly at the host-pathogen interface. We hope these additional data will help address the reviewer's concerns regarding Ppe1's localization.
Author response image 3.
FM4-64-stained rice leaf sheath inoculated with M. oryzae strain expressing Ppe1-GFP. Ppe1-GFP ring was positioned above the primary invasive hyphae. Scale bar = 5 µm.
Secondly, the authors assume Ppe1 is required for host infection due to its association with the peg. However, its role in infection is minor. The majority of appressoria produced by the mutant strain penetrate host cells and elaborate invasive hyphae, and lesion sizes are only marginally reduced compared to WT (in fact, the lesion density of the 70-15 WT strain itself seems reduced compared to what would be expected from this strain). The authors did not analyze the lesions for spores to confirm that the mutant strains were non-pathogenic (non-pathogenic mutants sometimes form small pinprick-like lesions that do not sporulate). Thus, the pathogenicity phenotype of the knockout mutant is weak, which could contribute to the inability to accurately define the molecular and cellular function of Ppe1.
We appreciate the reviewer’s comments. To ensure the reliability of our findings, we conducted spray inoculation experiments with multiple independent repeats. Our results consistently demonstrated that deletion of the PPE1 gene significantly attenuates the virulence of M. oryzae. Further analysis of lesion development and sporulation in the Δ_ppe1_ mutant revealed that it retains the ability to produce conidia. To validate these observations, we generated a PPE1 knockout in the wild-type reference strain Guy11. Similarly, we observed a significant decrease in the pathogenicity of the Δ_ppe1_ mutants generated from the wild-type Guy11 strain compared to Guy11 in the spray assay (Fig S2). These results collectively indicate the importance of Ppe1 in the pathogenicity of M. oryzae to rice.
In summary, it is important that the role of Ppe1 in infection be determined.
Reviewer #2 (Public review):
The article focuses on the study of Magnaporthe oryzae, the fungal pathogen responsible for rice blast disease, which poses a significant threat to global food security. The research delves into the infection mechanisms of the pathogen, particularly the role of penetration pegs and the formation of a penetration ring in the invasion process. The study highlights the persistent localization of Ppe1 and its homologs to the penetration ring, suggesting its function as a structural feature that facilitates the transition of penetration pegs into invasive hyphae. The article provides a thorough examination of the infection process of M. oryzae, from the attachment of conidia to the development of appressoria and the formation of invasive hyphae. The discovery of the penetration ring as a structural element that aids in the invasion process is a significant contribution to the understanding of plant-pathogen interactions. The experimental methods are well-documented, allowing for reproducibility and validation of the results.
We sincerely appreciate the thoughtful and insightful evaluation of our work. Thank you for recognizing the significance of our findings regarding the penetration ring and the functional role of Ppe1 during host invasion.
Recommendations for the authors:
Reviewer #1 (Recommendations for the authors):
Line 48: "after appressorium- or transpressorium-mediated penetration of plant cell wall" - transpressoria do not penetrate the plant cell wall.
Thank you for your valuable suggestion. For improved clarity, we have rephrased the sentence as follows: In this study, we showed that a penetration ring is formed by penetration pegs after appressorium-mediated penetration of plant cell wall.
Line 143: "approximately 25% of the 143 appressoria formed by the Δppe1 mutant had no penetration peg" - It is not possible to see the penetration peg by confocal microscopy.
Thank you for your valuable suggestion. We have revised the sentence as follows: In contrast, approximately 25% of the appressoria formed by the Δ_ppe1_ mutant had no penetration.
Line 159: "inner cycle" -should be inner circle?
We gratefully acknowledge the reviewer's careful reading. The typographical error has been corrected throughout the revised manuscript.
Line 255: "These results indicate that initiation of penetration peg formation is necessary for the formation of the penetration ring." Actually, more precisely, they indicate that penetration is necessary.
We appreciate this suggestion and have revised the text to be more concise: These results indicate that penetration is necessary for the formation of the penetration ring.
Line 282: "unlike subcellular localizations of other effectors"- is this an effector if no plant targets are known?
We appreciate this suggestion and have revised the text as follows: unlike subcellular localizations of Bas4, Slp1, Pwl2, and AvrPiz-t.
Line 299: "it may function as a novel physical structure for anchoring penetration pegs on the surface of plant cytoplasm membrane after cell wall penetration" - an interaction with the plant plasma membrane was not shown and this is speculative.
We have provided new evidence to show the spatial positioning of Ppe1-mCherry ring with the rice plasma membrane (see figure S8)
Line 301: "It is also possible that this penetration ring functions as a collar or landmark that is associated with the differentiation of penetration pegs (on the surface of cytoplasm membrane) into primary invasive hyphae enveloped in the EIHM cytoplasm membrane (Figure 7)." The alternative conclusions for Ppe1 function, either interacting with host membranes or acting as a developmental landmark, need to be resolved here.
We appreciate this suggestion and have revised the text as follows: It is also possible that this penetration ring functions as a collar that is associated with the differentiation of penetration pegs into primary invasive hyphae enveloped in the EIHM (Figure 7).
Line 317: "is likely a structural feature or component for signaling the transition of penetration pegs to invasive hyphae",- if the authors think Ppe1 has these roles, why do they refer to Ppe1 as an effector?
Many thanks for these comments. We have revised this and refer to Ppe1 as a secreted protein throughout the revised manuscript.
Line 337: "After the penetration of plant cell wall, the penetration ring may not only function as a physical structure but also serve as an initial effector secretion site for the release of specific effectors to overcome plant immunity in early infection stages"- which is it? Also, no evidence is provided to suggest it is a platform for effector secretion.
We sincerely appreciate your valuable suggestion. We have revised this sentence as follows: After the penetration of plant cell wall, the penetration ring may not only function as a physical structure but also serve as a secretion site for the release of specific proteins to overcome plant immunity during the early infection stages.
Reviewer #2 (Recommendations for the authors):
(1) While the study suggests the penetration ring as a structural feature, it remains unclear whether it also serves as a secretion site for effectors. Further exploration of this aspect would strengthen the conclusions.
We thank the reviewer for this useful suggestion. In this study, we demonstrated that Ppe1 proteins form a distinct penetration ring structure at the site where the penetration peg contacts the plant plasma membrane prior to differentiation into primary invasive hyphae (Figs. 2 and 7). Thus, we reasoned that penetration ring may function as a novel physical structure. Notably, additional Ppe family members (Ppe2, Ppe3, and Ppe5) were also found to localize to this penetration ring (Fig. 6B), suggesting that it also serves as a secretion site for releasing proteins. To test whether Ppe1 and Ppe2 label to the same site, we analyzed the colocalization between Ppe1-GFP and Ppe2-mCherry. The results showed that Ppe1-GFP and Ppe2-mCherry are well colocalized (Author response image 4). This study primarily focuses on the discovery and characterization of the penetration ring. The potential role of this structure in effector translocation will be investigated in future studies.
Author response image 4.
Ppe1 co-localizes with Ppe2 at the penetration ring in M. oryzae. Line graphs were generated at the directions pointed by the white arrows. Scale bar = 2μm.
(2) The article could benefit from a discussion on the broader implications of these findings for developing resistant crop varieties or new fungicidal strategies.
We have incorporated this discussion as suggested (lines 358-360).
(3) What is the significance of the formation of the penetration ring in the pathogenicity of the rice blast fungus? Or, how does it assist the fungus in its infection process?
Our findings have several significant implications. First, we believe that the discovery of the penetration ring as a novel physical structure associated with the differentiation of invasive hyphae represents a breakthrough in plant-pathogen interactions that will be of interest to fungal biologists, pathologists and plant biologists. Secondly, our study presents new role of the peg as a specialized platform for secretory protein deployment, in addition to its commonly known role as a physical penetration tool for the pathogen. Thirdly, we identify Ppe1 as a potential molecular target for controlling the devastating rice blast disease, as Ppe homologs are absent in plants and mammals. We have incorporated this discussion in the revised manuscript (lines 354-362).
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www.bbc.co.uk www.bbc.co.uk
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Welcome to the BBC
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Example Domain This domain is for use in illustrative examples in documents. You may use this domain in literature without prior coordination or asking for permission. More information...
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classics.mit.edu classics.mit.edu
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Wide o'er man my realm extends, and proud the name that I, the goddess Cypris, bear, both in heaven's courts and 'mongst all those who dwell within the limits of the sea and the bounds of Atlas, beholding the sun-god's light; those that respect my power I advance to honour, but bring to ruin all who vaunt themselves at me. For even in the race of gods this feeling finds a home, even pleasure at the honour men pay them. And the truth of this I soon will show; for that son of Theseus, born of the Amazon, Hippolytus, whom holy Pittheus taught, alone of all the dwellers in this land of Troezen, calls me vilest of the deities. Love he scorns, and, as for marriage, will none of it; but Artemis, daughter of Zeus, sister of Phoebus, he doth honour, counting her the chief of goddesses, and ever through the greenwood, attendant on his virgin goddess, he clears the earth of wild beasts with his fleet hounds, enjoying the comradeship of one too high for mortal ken. 'Tis not this I grudge him, no! why should I? But for his sins against me
Annotation by: [Your Full Name] CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Linguistic and Cultural Context: Aphrodite talks in a super fancy way here. She talks and acts like a queen to make herself sound more powerful. This is because she’s a goddess, and in Greek plays, gods were always shown as being really important. The way she talks is all about showing off her power. She says she can help people who respect her or destroy people who don’t. This kind of serious, dramatic language is normal for Greek gods in plays because it makes them seem way bigger and more important than normal people.
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Wide o'er man my realm extends, and proud the name that I, the goddess Cypris, bear, both in heaven's courts and 'mongst all those who dwell within the limits of the sea and the bounds of Atlas, beholding the sun-god's light; those that respect my power I advance to honour, but bring to ruin all who vaunt themselves at me.
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Comparative Insight: In this quote, Aphrodite declares her vast influence over both mortals and gods, emphasizing that she rewards those who honor her and punishes those who don't. This showcases her as a powerful female deity who demands respect and can control the fates of individuals. Her power over love and desire contrasts with Hippolytus' self-control and rejection of passion, highlighting the different ways power is portrayed in the play.
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Wide o'er man my realm extends, and proud the name that I, the goddess Cypris, bear, both in heaven's courts and 'mongst all those who dwell within the limits of the sea and the bounds of Atlas, beholding the sun-god's light; those that respect my power I advance to honour, but bring to ruin all who vaunt themselves at me.
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Analysis: In this quote, Aphrodite talks about how powerful she is. She controls love and desire everywhere, and she makes it clear that if people respect her, she will help them. But if they ignore her or disrespect her, she will punish them. This shows that even though she is a goddess of love, she is not just kind and gentle but that she can also be dangerous if people make her angry. This makes her a really powerful female character in the story because she can control people’s feelings and lives.
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www.perseus.tufts.edu www.perseus.tufts.edu
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I honor those who reverence my power, but I lay low all those who think proud thoughts against me. For in the gods as well one finds this trait: they enjoy receiving honor from mortals.
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Analysis: In this quote, Aphrodite talks about how she rewards people who respect her but punishes anyone who disrespects her. This shows how powerful she is because everyone has to listen to her, even though she’s a goddess of love. It also shows how women, especially goddesses, were expected to be respected but could also be blamed if something went wrong.
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www.pelister.org www.pelister.org
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He waswise, lie saw mysteries and knew secret things, he brought us a tale of the daysbefore the flood.
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Linguistic and Cultural Context: Kovacs’ version is written in modern and clear English, which makes it easy to understand and focuses on Gilgamesh’s journey. Sandars’ version is written in a more poetic style, making him look like a hero. These two styles show how translators can change the way we see a character, depending on whether they want him to look like a brave man or a famous hero.
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e went on a long journey, was weary, worn-out with labour,returning he rested, he engraved on a stone the whole story
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Comparative Insight: Both versions show Gilgamesh as a hero, but they focus on different things. Kovacs’ version shows him as someone who goes on a tough journey and learns a lot, while Sandars’ version makes him look like a famous legend whose story should be told to everyone. This connects to gender politics because it shows two ways of being a "great man", first is about bravery and wisdom, and the other is about being remembered.
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WILL proclaim to the world the deeds of Gilgamesh. This was the man to whomall things were known; this was the king who knew the countries of the world. He waswise, lie saw mysteries and knew secret things, he brought us a tale of the daysbefore the flood. He went on a long journey, was weary, worn-out with labour,returning he rested, he engraved on a stone the whole story.
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Analysis: In this version, Gilgamesh is shown as a hero who had come back from a journey and shares his stories from these adventures. This connects to gender politics because it shows how men were expected to be strong leaders who were remembered for their work and achievements.
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people.uncw.edu people.uncw.edu
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He went on a distant journey, pushing himself to exhaustion,but then was brought to peace
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Linguistic and Cultural Context: Kovacs’ version is written in modern and clear English, which makes it easy to understand and focuses on Gilgamesh’s journey. Sandars’ version is written in a more poetic style, making him look like a hero. These two styles show how translators can change the way we see a character, depending on whether they want him to look like a brave man or a famous hero.
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He carved on a stone stela all of his toils,and built the wall of Uruk-Haven,the wall of the sacred Eanna Temple, the holy sanctuary
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Comparative Insight: Both versions show Gilgamesh as a hero, but they focus on different things. Kovacs’ version shows him as someone who goes on a tough journey and learns a lot, while Sandars’ version makes him look like a famous legend whose story should be told to everyone. This connects to gender politics because it shows two ways of being a "great man", first is about bravery and wisdom, and the other is about being remembered.
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He saw the Secret, discovered the Hidden,he brought information of (the time) before the Flood.He went on a distant journey, pushing himself to exhaustion,but then was brought to peace
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211 In this version, Gilgamesh is shown as a hero who goes on a long journey, learns a lot, and brings back stories from the past. This makes him look like the a good hero where he has characteristics of someone who is brave, curious, and always trying to learn more. This connects to gender politics because it shows how men were expected to be strong, adventurous, and wise.
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www.poetryfoundation.org www.poetryfoundation.org
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“This was my thought, when my thanes and I bent to the ocean and entered our boat, that I would work the will of your people fully, or fighting fall in death, in fiend’s gripe fast. I am firm to do an earl’s brave deed, or end the days of this life of mine in the mead-hall here.”
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Linguistic and Cultural Context: Hall’s translation is from the 1800s, so it uses older and fancier words to describe Beowulf and how his characteristics make him a hero. Gummere’s translation is from the early 1900s and is easier to read using more of modern texts and descriptions. These differences show how ideas of heroism and masculinity can change over time, even though Beowulf is always a strong, brave hero.
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I would work the will of your people fully, or fighting fall in death,
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Comparative Insight: Both versions show Beowulf as a brave and respectful hero, but Hall’s version is more poetic, which makes Beowulf seem like a legendary figure. Gummere’s version is simpler and makes Beowulf seem more like a real person narrating the story. Both connect to gender politics by highlighting how a hero must be strong but also respectful.
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This was my thought, when my thanes and I bent to the ocean and entered our boat, that I would work the will of your people fully, or fighting fall in death,
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Analysis: In this quote, Beowulf shows his bravery by talking about how he and his men sailed across the sea to help Hrothgar and his people, knowing that they might die. This is a big part of gender politics because it shows the traditional idea of masculinity of being strong, fearless, and willing to sacrifice yourself for honor.
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www.perseus.tufts.edu www.perseus.tufts.edu
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multitude of dreams at night
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Linguistic and Cultural Context: Potter's version is more descriptive in her feelings of her son's departure. It shows more of an emotional side of the story. Smyth's version tells the story like a book where it does not show as much emotion and gets to the point. These two stories show how different emotions can be shown of the same character based on different writing.
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I have been haunted by a multitude of dreams at night since the time when my son, having despatched his army, departed with intent to lay waste the land of the Ionians. But never yet have I beheld so distinct a vision [180] as that of the last night. This I will describe to you.
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Comparative Insight: Both versions show Atossa being upset, but in different ways. In Potter’s version, she’s emotional and scared, which makes her seem vulnerable. In Smyth’s version, she’s more controlled, which makes her look strong.
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I have been haunted by a multitude of dreams at night since the time when my son, having despatched his army, departed with intent to lay waste the land of the Ionians.
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Analysis: This version of Atossa is different. She’s still worried, but instead of showing it publicly, she keeps her feelings inside. She instead tells us about the dreams she has about her son. This connects to the view of women as she is showing us a different version of her being more strong as she isn't showing her emotions publically but has dreams instead.
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classics.mit.edu classics.mit.edu
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Haunting my dreams, how plainly did you show
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Linguistic and Cultural Context: Potter's version is more descriptive in her feelings of her son's departure. It shows more of an emotional side of the story. Smyth's version tells the story like a book where it does not show as much emotion and gets to the point. These two stories show how different emotions can be shown of the same character based on different writing.
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Ah me, what sorrows for our ruin'd host Oppress my soul! Ye visions of the night
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Analysis: In this version, Atossa is emotional as she talks about nightmares that keep haunting her, and it shows how worried she is for her son and the Persian army. It shows a traditional view of women that show emotions as she shows her emotions of sad, fear, anxious, etc when it comes to her son and the people.
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Ah me, what sorrows for our ruin'd host Oppress my soul! Ye visions of the night Haunting my dreams, how plainly did you show These ills!-You set them in too fair a light.
Annotation by: Jatnna Sanchez CC License: CC BY-NC-SA 4.0 Tag: #SP2025-Lit211
Comparative Insight: Both versions show Atossa being upset, but in different ways. In Potter’s version, she’s emotional and scared, which makes her seem vulnerable. In Smyth’s version, she’s more controlled, which makes her look strong.
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www.biorxiv.org www.biorxiv.org
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Author response:
The following is the authors’ response to the original reviews
Public Reviews:
Reviewer #1 (Public review):
Summary:
This study puts forth the model that under IFN-B stimulation, liquid-phase WTAP coordinates with the transcription factor STAT1 to recruit MTC to the promoter region of interferon-stimulated genes (ISGs), mediating the installation of m<sup>6</sup>A on newly synthesized ISG mRNAs. This model is supported by strong evidence that the phosphorylation state of WTAP, regulated by PPP4, is regulated by IFN-B stimulation, and that this results in interactions between WTAP, the m<sup>6</sup>A methyltransferase complex, and STAT1, a transcription factor that mediates activation of ISGs. This was demonstrated via a combination of microscopy, immunoprecipitations, m<sup>6</sup>A sequencing, and ChIP. These experiments converge on a set of experiments that nicely demonstrate that IFN-B stimulation increases the interaction between WTAP, METTL3, and STAT1, that this interaction is lost with the knockdown of WTAP (even in the presence of IFN-B), and that this IFN-B stimulation also induces METTL3-ISG interactions.
Strengths:
The evidence for the IFN-B stimulated interaction between METTL3 and STAT1, mediated by WTAP, is quite strong. Removal of WTAP in this system seems to be sufficient to reduce these interactions and the concomitant m<sup>6</sup>A methylation of ISGs. The conclusion that the phosphorylation state of WTAP is important in this process is also quite well supported.
Weaknesses:
The evidence that the above mechanism is fundamentally driven by different phase-separated pools of WTAP (regulated by its phosphorylation state) is weaker. These experiments rely relatively heavily on the treatment of cells with 1,6-hexanediol, which has been shown to have some off-target effects on phosphatases and kinases (PMID 33814344).
Given that the model invoked in this study depends on the phosphorylation (or lack thereof) of WTAP, this is a particularly relevant concern.
We are grateful for the reviewer’s positive comment and constructive feedback. 1,6-hexanediol (hex) was considered an inhibitor of hydrophobic interaction, thereby capable of dissolving protein phase separation condensates. Hex (5%-10% w/v) was still widely used to explore the phase separation characteristic and function on various protein, including some phosphorylated proteins such as pHSF1, or kinases such as NEMO1-3. Since hydrophobic interactions involved in various types of protein-protein interaction, the off-target effects of hex were inevitable. It has been reported that hex impaired RNA polymerase II CTD-specific phosphatase and kinase activity at 5% concentration4, which led to the reviewer’s concern. In response to this concern, we investigated the phosphorylation level of WTAP under hex concentration gradient treatment. Surprisingly, we found that both 2% and 5% hex maintained the PPP4c-mediated dephosphorylation level of WTAP but still led to the dissolution of WTAP LLPS condensates (Figure 5-figure supplement 1H; Author response image 1), indicating that hex dispersed WTAP phase separation in a phosphorylation-independent manner. Consistent with our findings, Ge et al. used 10% hex to dissolve WTAP phase separation condensates5. Additionally, we found the phosphorylation level of STAT1 was not affected by both 2% and 5% hex, revealing the off-target and impairment function of hex on kinases or phosphatases might not be universal (Figure 5-figure supplement 1H). Collectively, since the 5% hex we used did not influence the de-phosphorylation event of WTAP, function of WTAP LLPS mediating interaction between methylation complex and STAT1 revealed by our results was independent from its phosphorylation status.
Author response image 1.
mCherry-WTAP-rescued HeLa cells were treated with 10 ng/mL IFN-β together with or without 2% or 5% hex and 20 μg/mL digitonin for 1 hour or left untreated. Phase separation of mCherry-WTAP was observed through confocal microscopy. The number of WTAP condensates that diameter over 0.4 μm of n = 20 cells were counted through ImageJ and shown. Scale bars indicated 10 μm. All error bars, mean values ± SD, P-values were determined by unpaired two-tailed Student’s t-test of n = 20 cells in (B). For (A), similar results were obtained for three independent biological experiments.
Related to this point, it is also interesting (and potentially concerning for the proposed model) that the initial region of WTAP that was predicted to be disordered is in fact not the region that the authors demonstrate is important for the different phase-separated states.
A considerable number of proteins undergo phase separation via interactions between intrinsically disordered regions (IDRs). IDR contains more charged and polar amino acids to present multiple weakly interacting elements, while lacking hydrophobic amino acids to show flexible conformations6. In our study, we used PLAAC websites (http://plaac.wi.mit.edu/) to predict IDR domain of WTAP, and a fragment (234-249 amino acids) was predicted as prion-like domain (PLD). However, deletion of this fragment failed to abolish the phase separation properties of WTAP, which might be the main confusion to reviewers. To explain this issue, we checked the WTAP structure (within part of MTC complex) from protein data bank (https://www.rcsb.org/structure/7VF2) and found that the prediction of IDR has been renewed due to the update of different algorithm. IDR of WTAP expanded to 245-396 amino acids, encompassing the entire CTD region. Our results demonstrate that the CTD was critical for WTAP LLPS, as CTD deficiency significantly inhibited the formation of liquid condensates both in vitro and in cells. Also, phosphorylation sites on CTD were important for the phase transition of WTAP. These observations highlight the phosphorylation status on CTD region as a key driving force of phase separation, consistent with the established role of IDR in regulating LLPS. We have revised our description on WTAP IDR in our article following the reviewers’ suggestion.
Taking all the data together, it is also not clear to me that one has to invoke phase separation in the proposed mechanism.
In this article, we observed that WTAP underwent phase transition during virus infection and IFN-β treatment, and proposed a novel mechanism whereby post translational modification (PTM)-driven WTAP LLPS was required for the m<sup>6</sup>A modification of ISG mRNAs. To verify the hypothesis, we first demonstrated the relationship between PTM and phase separation of WTAP. We constructed WTAP 5ST-D and 5ST-A mutant to mimic WTAP phosphorylation and dephosphorylation status respectively, and figured out that dephosphorylated WTAP underwent LLPS. We also found that PPP4 was the main phosphatase to regulate WTAP dephosphorylation. To further investigation, we introduced the potent PPP4 inhibitor, fostriecin. Consistent with our findings in PPP4 deficient model, fostriecin treatment significantly inhibited the IFN-β-induced dephosphorylation of WTAP and disrupted its LLPS condensates, indicating that PPP4 was the key phosphatase recruited by IFN-β to regulate WTAP, confirming that PTM governs WTAP LLPS dynamics (Figure 2-figure supplement 1C and H). Furthermore, fostriecin-induced impairment of WTAP phosphorylation and phase separation correlated with reduced m<sup>6</sup>A modification level and elevated ISGs expression level (Figure 4C and Figure 4-figure supplement 1E). These findings together emphasized that dephosphorylation is required for WTAP LLPS.
As for the function of WTAP LLPS, we assumed that WTAP might undergo LLPS to sequester STAT1 together with m<sup>6</sup>A methyltransferase complex (MTC) for mediating m<sup>6</sup>A deposition on ISG mRNAs co-transcriptionally under IFN-β stimulation. Given that hex dissolved WTAP LLPS condensates without affecting dephosphorylation status (Figure 5-figure supplement 1H; Author response image 1), various experiments we performed previously actually confirmed the critical role of WTAP LLPS during m<sup>6</sup>A modification (Figure 4A), as well as the mechanism that WTAP phase separation enhanced the interaction between MTC and STAT1 (Figure 5E-F). Subsequent to reviewer’s comments, more experiments were conducted for further validation. We found the WTAP liquid condensates formed by wild type (WT) WTAP or WTAP 5ST-A mutant (which mimics dephosphorylated-WTAP) could be dissembled by hex, which also led to the impairment of the interaction between STAT1, METTL3 and WTAP (Figure 5-figure supplement 1E). In addition, in vitro experiments demonstrated that hex treatment significantly disrupted the interaction between recombinant GFP-STAT1 and mCherry-WTAP which expressed in the E. coli system (Figure 5F and Figure 5-figure supplement 1G). Notably, this prokaryotic expression system lacks endogenous phosphorylation machinery, resulting in non-phosphorylated mCherry-WTAP. For further validation, we performed the interaction of WTAP WT or 5ST-A with the promoter regions of ISG as well as the m<sup>6</sup>A modification of ISG mRNAs were attenuated by WTAP LLPS dissolution (Figure 4E and Figure 6E). These findings together revealed that WTAP LLPS were the critical mediators of the STAT1-MTC interactions, ISG promoter regions binding and the co-transcription m<sup>6</sup>A modification.
Collectively, our results demonstrated that IFN-β treatment recruited PPP4c to dephosphorylate WTAP, thereby driving the formation of WTAP liquid condensates which were essential for facilitating STAT1-MTC interaction and m<sup>6</sup>A deposition, subsequently mediated ISG expression. Since we revealed a strong association between PTM-regulated WTAP phase transition and its m<sup>6</sup>A modification function, WTAP LLPS was a novel and functionally distinct mechanism that must be reckoned with in this study.
Author response image 2.
Wild type (WT) WTAP or 5ST-A mutant-rescued WTAP<sup>sgRNA</sup> THP-1-derived macrophages are stimulated with or without with 10 ng/mL IFN-β together followed with 2% or 5% 1,6-hexanediol (hex) and 20 μg/mL digitonin for 1 hour or left untreated. antibody and imaged using confocal microscope. Scale bars indicated 10 μm.
Reviewer #2 (Public review):
In this study, Cai and colleagues investigate how one component of the m<sup>6</sup>A methyltransferase complex, the WTAP protein, responds to IFNb stimulation. They find that viral infection or IFNb stimulation induces the transition of WTAP from aggregates to liquid droplets through dephosphorylation by PPP4. This process affects the m<sup>6</sup>A modification levels of ISG mRNAs and modulates their stability. In addition, the WTAP droplets interact with the transcription factor STAT1 to recruit the methyltransferase complex to ISG promoters and enhance m<sup>6</sup>A modification during transcription. The investigation dives into a previously unexplored area of how viral infection or IFNb stimulation affects m<sup>6</sup>A modification on ISGs. The observation that WTAP undergoes a phase transition is significant in our understanding of the mechanisms underlying m<sup>6</sup>A's function in immunity. However, there are still key gaps that should be addressed to fully accept the model presented.
Major points:
(1) More detailed analyses on the effects of WTAP sgRNA on the m<sup>6</sup>A modification of ISGs:
a. A comprehensive summary of the ISGs, including the percentage of ISGs that are m<sup>6</sup>A-modified. merip-isg percentage
b. The distribution of m<sup>6</sup>A modification across the ISGs. Topology
c. A comparison of the m<sup>6</sup>A modification distribution in ISGs with non-ISGs. Topology
In addition, since the authors propose a novel mechanism where the interaction between phosphorylated STAT1 and WTAP directs the MTC to the promoter regions of ISGs to facilitate co-transcriptional m<sup>6</sup>A modification, it is critical to analyze whether the m<sup>6</sup>A modification distribution holds true in the data.
We appreciate the reviewer’s summary of our manuscript and the constructive assessment. We have conducted the related analysis accordingly to present the m<sup>6</sup>A modification in ISGs in our model as reviewers suggested. Our results showed that about 64.29% of core ISGs were m<sup>6</sup>A modified under IFN-β stimulation (Figure 3-figure supplement 1B; Figure 3G), which was consistent with the similar percentage in previous studies[7,8]. The m<sup>6</sup>A distribution of the ISGs transcripts including IFIT1, IFIT2, OAS1 and OAS2 was validated (Figure 3-figure supplement 1H).
Generally, m<sup>6</sup>A deposition preferentially located in the vicinity of stop codon, while m<sup>6</sup>A modification was highly dynamic under different cellular condition. However, we compared the topology of m<sup>6</sup>A deposition of ISGs with non-ISGs, and found that m<sup>6</sup>A modification of ISG mRNAs showed higher preference of coding sequences (CDS) localization compared to global m<sup>6</sup>A deposition (Figure 3H). Similarly, various researches uncovered the m<sup>6</sup>A deposition regulated by co-transcriptionally m<sup>6</sup>A modification preferred to locate in the CDS [9-11]. Since our results of m<sup>6</sup>A modification distribution of ISGs was consistent with the co-transcriptional m<sup>6</sup>A modification characteristics, we believed that our hypothesis and results were correlated and consistent.
(2) Since a key part of the model includes the cytosol-localized STAT1 protein undergoing phosphorylation to translocate to the nucleus to mediate gene expression, the authors should focus on the interaction between phosphorylated STAT1 and WTAP in Figure 4, rather than the unphosphorylated STAT1. Only phosphorylated STAT1 localizes to the nucleus, so the presence of pSTAT1 in the immunoprecipitate is critical for establishing a functional link between STAT1 activation and its interaction with WTAP.
Thank you for the constructive comments. As we showed in Figure 4, we found the enhanced interaction between phase-separated WTAP and the nuclear-translocated STAT1 which were phosphorylated under IFN-β stimulation, indicating the importance of phosphorylation of STAT1. We repeated the immunoprecipitation experiments to clarify the function of pSTAT1 in WTAP interaction. Our results showed that IFN-β stimulation induced the interaction of WTAP with both pSTAT1 and STAT1 (Figure 5-figure supplement 1C), indicating that most of the WTAP-associated STAT1 was phosphorylated. Taken together, our data proved that LLPS WTAP bound with nuclear-translocated pSTAT1 under IFN-β stimulation.
(3) The authors should include pSTAT1 ChIP-seq and WTAP ChIP-seq on IFNb-treated samples in Figure 5 to allow for a comprehensive and unbiased genomic analysis for comparing the overlaps of peaks from both ChIP-seq datasets. These results should further support their hypothesis that WTAP interacts with pSTAT1 to enhance m<sup>6</sup>A modifications on ISGs.
Thank you for raising this thoughtful comment. In this study, MeRIP-seq and RNA-seq along with immunoprecipitation and immunofluorescence experiments supported that phase transition of WTAP enhanced its interaction to pSTAT1, thus mediating ISGs m<sup>6</sup>A modification and expression by enhancing its interaction with nuclear-translocated pSTAT1 during virus infection and IFN-β stimulation. However, how WTAP-mediated m<sup>6</sup>A modification was related to STAT1-mediated transcription remained unclear. Several researches have revealed the recruitment of m<sup>6</sup>A methyltransferase complex (MTC) to transcription start sites (TSS) of coding genes and R-loop structure by interacting with transcriptional factors STAT5B, SMAD2/3, DNA helicase DDX21, indicating the engagement of MTC mediated m<sup>6</sup>A modification on nascent transcripts at the very beginning of transcription [11-13]. These researches inspired us that phase-separated WTAP could be recruited to the ISG promoter regions via interacting with nuclear-translocated pSTAT1. To validate this mechanism, we have conducted ChIP-qPCR experiments targeting STAT1 and WTAP, revealed that IFN-β induced the comparable recruitment dynamics of both STAT1 and WTAP to ISG promoter regions (Figure 6A-B). Notably, STAT1 deficiency significantly abolished the bindings between WTAP and ISG promoter regions (Figure 6C). These findings established nuclear-translocated STAT1-dependent recruitment of phase separated WTAP and ISG promoter region, substantiated our hypothesis within the current study. We totally agree that ChIP-seq data will be more supportive to explore the mechanism in depth. We will continuously focus on the whole genome chromatin distribution of WTAP and explore more functional effect of transcriptional factor-dependent WTAP-promoter regions interaction in the future.
Minor points:
(1) Since IFNb is primarily known for modulating biological processes through gene transcription, it would be informative if the authors discussed the mechanism of how IFNb would induce the interaction between WTAP and PPP4.
Protein phosphatase 4 (PPP4) is a multi-subunit serine/threonine phosphatase complex that participates in diverse biologic process, including DDR, cell cycle progression, and apoptosis[14]. Several signaling pathway such as NF-κB and mTOR signaling, can be regulated by PPP4. Previous research showed that deficiency of PPP4 enhanced IFN-β downstream signaling and ISGs expression, which was consistent with our findings that knockdown of PPP4C impaired WTAP-mediated m<sup>6</sup>A modification, enhanced the ISGs expression[15,16]. Since there was no significant enhancement in PPP4 expression level during 0-3 hours of IFN-β stimulation in our results, we explored the PTM that may influence the protein-protein interaction, such as ubiquitination. Intriguingly, we found the ubiquitination level of PPP4 was enhanced after IFN-β stimulation, which may affect the interaction between PPP4 and WTAP (Author response image 3). Further investigation between PPP4 and WTAP will be conducted in our future study.
Author response image 3.
HEK 293T transfected with HA-ubiquitin (HA-Ub) and Flag-PPP4 were treated with 10 ng/mL IFN-β or left untreated. Whole cell lysate (WCL) was collected and immunoprecipitation (IP) experiment using anti-Flag antibody was performed, followed with immunoblot. Similar results were obtained for three independent biological experiments.
(2) The authors should include mCherry alone controls in Figure 1D to demonstrate that mCherry does not contribute to the phase separation of WTAP. Does mCherry have or lack a PLD?
According to the crystal structure of mCherry protein in protein structure database RCSB-PDB, mCherry protein presents as a β-barrel protein, with no IDRs or multivalent interaction domains including PLD, indicating that mCherry protein has no capability to undergo phase separation. This characteristic makes it a suitable protein to tag and trace the localization or expression levels of proteins, and a negative control for protein phase separation studies. As the reviewer suggested, we include mCherry alone controls in the revised version (Figure 1D).
(3) The authors should clarify the immunoprecipitation assays in the methods. For example, the labeling in Figure 2A suggests that antibodies against WTAP and pan-p were used for two immunoprecipitations. Is that accurate?
Due to the lack of phosphorylated-WTAP antibody, the detection of phosphorylation of WTAP was conducted by WTAP-antibody-mediated immunoprecipitation. We conducted immunoprecipitation to pull-down WTAP protein by WTAP antibody, then used antibody against phosphoserine/threonine/tyrosine (pan-p) to detect the phosphorylation level of WTAP. To avoid the misunderstanding, we have modified the description from pan-p to pWTAP (pan-p) in figures and revised the figure legends.
(4) The authors should include overall m<sup>6</sup>A modification levels quantified of GFP<sup>sgRNA</sup> and WTAP<sup>sgRNA</sup> cells, either by mass spectrometry (preferably) or dot blot.
We thank reviewer for raising these useful suggestions. As we showed in Figure 3F and J-K, the m<sup>6</sup>A modification event and degradation of ISG mRNAs were significantly depleted in WTAP<sup>sgRNA</sup> cell lines, indicating that function of WTAP was deficient. Thus, we used the WTAP<sup>sgRNA</sup> #2 cell line to perform most of our experiment. Furthermore, we also found 46.4% of global m<sup>6</sup>A modification was decreased in WTAP<sup>sgRNA</sup> THP-1 cells than that of control cells with or without IFN-β stimulation (Author response image 4), further validating that level of m<sup>6</sup>A modification was significantly affected in WTAP<sup>sgRNA</sup> cells. Taken together, our data confirmed that m<sup>6</sup>A methyltransferase activity was efficiently inhibited in our WTAP<sup>sgRNA</sup> cells.
Author response image 4.
Control (GFP<sup>sgRNA</sup>) and WTAP<sup>sgRNA</sup> #2 THP-1-derived macrophages were treated with 10 ng/mL IFN-β for 4 hours. Global m<sup>6</sup>A level was detected and quantified through ELISA assays. All error bars, mean values ± SEM, P-values were determined by two-way ANOVA test independent biological experiments.
Reviewer #3 (Public review):
Summary:
This study presents a valuable finding on the mechanism used by WTAP to modulate the IFN-β stimulation. It describes the phase transition of WTAP driven by IFN-β-induced dephosphorylation. The evidence supporting the claims of the authors is solid, although major analysis and controls would strengthen the impact of the findings. Additionally, more attention to the figure design and to the text would help the reader to understand the major findings.
Strength:
The key finding is the revelation that WTAP undergoes phase separation during virus infection or IFN-β treatment. The authors conducted a series of precise experiments to uncover the mechanism behind WTAP phase separation and identified the regulatory role of 5 phosphorylation sites. They also succeeded in pinpointing the phosphatase involved.
Weaknesses:
However, as the authors acknowledge, it is already widely known in the field that IFN and viral infection regulate m<sup>6</sup>A mRNAs and ISGs. Therefore, a more detailed discussion could help the reader interpret the obtained findings in light of previous research.
We are grateful for the positive comments and the unbiased advice by the reviewer. To interpret our findings in previous research, we have revised the manuscript carefully and added more detailed discussion on ISG mRNAs m<sup>6</sup>A modification during virus infection or IFN stimulation.
It is well-known that protein concentration drives phase separation events. Similarly, previous studies and some of the figures presented by the authors show an increase in WTAP expression upon IFN treatment. The authors do not discuss the contribution of WTAP expression levels to the phase separation event observed upon IFN treatment. Similarly, METTL3 and METTL14, as well as other proteins of the MTC are upregulated upon IFN treatment. How does the MTC protein concentration contribute to the observed phase separation event?
We thank reviewer for pointing out the importance of the concentration dependent phase transition. Previously, Ge et al. discovered that expression level of WTAP was up-regulated during LPS stimulation, thereby promoting WTAP phase separation ability and m<sup>6</sup>A modification, indicating that WTAP concentration indeed affects the phase separation event. In our article, we have generated the phase diagram with different concentration of recombinant mCherry-WTAP in vitro (Figure 1-figure supplement 1C). For in cells experiments, we constructed the TRE-mCherry-WTAP HeLa cells in which the expression of mCherry-WTAP was induced by doxycycline (Dox) in a dose-dependent manner (Author response image 5A). We detected the LLPS of mCherry-WTAP at different concentrations by increasing the doses of Dox, and found that WTAP automatically underwent LLPS only in an artificially high expression level (Author response image 5B). However, the cells we used to detect the WTAP phase separation in our article was mCherry-WTAP-rescued HeLa cells, in which mCherry-WTAP was introduced in WTAP<sup>sgRNA</sup> HeLa cells to stably express mCherry-WTAP. We had adjusted and verified the mCherry-WTAP expression level precisely to make the protein abundance similar to endogenous WTAP in wild type (WT) HeLa cells (Author response image 5C). We also repeated the IFN-β stimulation experiments and found no significant increase of WTAP protein level (Figure 5-figure supplement 1A). These findings indicated the phase separation of WTAP in our article was not artificially induced due to the extremely high protein expression level.
MTC protein expression level was crucial for m<sup>6</sup>A modification during virus infection event. Rubio et al. and Winkler et al. revealed that WTAP, METTL3 and METTL14 were up-regulated after 24 hours of HCMV infection[8,17]. Recently, Ge et al. proposed that WTAP protein was degraded after 12 hours of VSV and HSV stimulation5,18. However, these studies only focused on the virus infection event, how the MTC protein expression change after direct IFN-β stimulation was still unclear. Our study investigated the transition change of WTAP under IFNβ stimulation in a short time, we detected the expression level of MTC proteins within 6 hours of IFN-β treatment, and found no significant enhancement of WTAP, METTL3 or METTL14 protein level and mRNA level (Figure 5-figure supplement 1B and Figure 5-figure supplement 1A;). Our in vitro experiments showed that introducing CFP-METTL3 protein have no significant influence on WTAP phase separation (Figure 4H). Additionally, we performed in cells experiments and found that increased expression of METTL3 had no effect on WTAP phase separation event (Author response image 5D). Taken together, WTAP phase separation can be promoted by dramatically increased concentration of WTAP both in vitro and in cells, but the phase separation of WTAP under IFN-β stimulation in our study was not related with the expression level of MTC proteins.
Author response image 5.
(A) Immunoblot analysis of the expression of mCherry-WTAP in TRE-mCherry-WTAP HeLa cells treated with different doses of doxycycline (Dox). Protein level of mCherry-WTAP was quantified and normalized to β-actin of n=3 independent biological experiments. Results were obtained for three independent biological experiments. (B) Phase separation diagram of mCherry-WTAP in TRE-mCherry-WTAP HeLa cells treated with different doses of Dox were observed through confocal microscopy. Representative images for three independent biological experiments were shown in b while number of WTAP condensates that diameter over 0.4 μm of n=80 cells were counted and shown as medium with interquartile range. Dotted white lines indicated the location of nucleus. Scale bars indicated 10 μm. (C) Immunoblot analysis of the expression of endogenous WTAP in wildtype (WT) HeLa cells and mCherry-WTAP-rescued WTAP<sup>sgRNA</sup> HeLa cells. (D) mCherry-WTAP-rescued HeLa cells were transfected with 0, 200 or 400 ng of Flag-METTL3, followed with 10 ng/mL IFN-β for 1 hour or left untreated (UT). Phase separation of mCherry-WTAP was observed through confocal microscopy. The number of WTAP condensates that diameter over 0.4 μm of n = 20 cells were counted through ImageJ and shown. Representative images of n=20 cells were shown. All error bars, mean values ± SD were determined by unpaired two-tailed Student’s t-test of n = 3 independent biological experiments in (A). For (A, C), similar results were obtained for three independent biological experiments.
How is PP4 related to the IFN signaling cascade?
Both reviewer #2 and reviewer #3 raised a similar point on the relationship between PPP4 and IFN signaling. In short, protein phosphatase 4 (PPP4) participates in diverse biologic process, including DDR, cell cycle progression and apoptosis14 and several signaling pathway. Previous research showed that deficiency of PPP4 enhanced IFN-β downstream signaling and ISGs expression, which was consistent with our findings that knockdown of PPP4C impaired WTAP-mediated m<sup>6</sup>A modification, and enhanced the ISGs expression[15,16]. Since there was no significant enhancement in PPP4C expression level during 0-3 hours of IFN-β stimulation in our results, we tried to explore the post-translation modification which may influence the protein-protein interaction, such as ubiquitination. Intriguingly, we found the ubiquitination level of PPP4 was enhanced after IFN-β stimulation, which may affect the interaction between PPP4 and WTAP (Author response image 4). Investigation between PPP4 and WTAP will be conducted in our further study (also see minor points 1 of reviewer#2).
In general, it is very confusing to talk about WTAP KO as WTAPgRNA.
As we describe above, all WTAP-deficient THP-1 cells were generated using the CRISPR-Cas9 system with WTAP-specific sgRNA, and used bulk cells instead of the monoclonal knockout cell for further experiments. Since monoclonal knockout cells were not obtained, we refer it as WTAP<sup>sgRNA</sup> THP-1 cells rather than WTAP-KO THP-1 cells. We confirmed that WTAP expression was efficiently knocked down in WTAP<sup>sgRNA</sup> THP-1 cells, and the m<sup>6</sup>A modification level was significantly impaired (Figure 3I, Figure 3-figure supplement 1A and Author response image 4), which was suitable for mechanism investigation.
Recommendations for the authors:
Reviewer #1 (Recommendations for the authors):
Related to the points raised in 'weaknesses' above, if the authors want to claim that this mechanism is reliant on WTAP phase-separated states, additional controls should be done to demonstrate this. Based on the available data it seems that it is just as likely that the phosphorylation state of WTAP is mediating interactions with other factors and/or altering its subcellular localization, which may or may not be related to phase separation.
We are grateful for the constructive suggestions. As we showed in , Figure 5-figure supplement 1H; Author response image 1 along with the explanation above, 5% hex dispersed the phase separation condensates of WTAP without affecting its phosphorylation status, proving the interaction between STAT1 and methylation complex impaired by hex was depended on WTAP LLPS but not its phosphorylation status (Figure 5E-H). To further confirmed the recruitment of WTAP LLPS on ISG promoter region, we performed the immunoprecipitation and ChIP-qPCR experiments of wild type (WT) WTAP, 5ST-D and 5ST-A rescued THP-1 cells. Our results uncovered the interaction between de-phosphorylated-mimic WTAP mutant and STAT1, and its binding ability with ISG promoter regions were depleted by hex without affecting its phosphorylation status (Author response image 2, Figure 5-figure supplement 1 F, Figure 6E). Taken together, we identified the de-phosphorylation event that regulated phase transition of WTAP during IFN-β stimulation, and proposed that LLPS of WTAP mediated by dephosphorylation was the key mechanism to bind with STAT1 and mediate the m<sup>6</sup>A modification on ISG mRNAs.
Reviewer #2 (Recommendations for the authors):
The author order is different for the main text and the supplementary file.
Thank you for pointing out this mistake. We have corrected it in our revised version.
Reviewer #3 (Recommendations for the authors):
Signaling molecules? Do you mean RNA or protein post-translational modification?
Thank you for pointing out this problem. In this sentence, we mean the post-translational modification of signaling proteins. We have corrected this mistake in our revised version.
Line 145: Do you mean Figure 1C?
We have corrected it in our revised version.
Line 214: Are the cells KO for WTAP? Do you mean CRISPR KO? In general, it is easier to present WTAPgRNA as WTAPKO.
Thank you for the constructive suggestion. As we explained above, in this project, all WTAP-deficient THP-1 cells were generated using the CRISPR-Cas9 system with WTAP-specific sgRNA, and used bulk cells instead of the monoclonal knockout cells. We confirmed that WTAP expression was efficiently knocked down in WTAP<sup>sgRNA</sup> THP-1 cells, and the m<sup>6</sup>A modification level was significantly impaired (Figure 3I, Figure3-figure supplement 1A and Author response image 4). Since monoclonal knockout cells were not obtained, we refer it as WTAP<sup>sgRNA</sup> THP-1 cells rather than WTAP-KO THP-1 cells.
Line 221: WTAP KO has no effect on the expression level of transcription factors?
Thank you for pointing out the uncritical expression. We have corrected this in our revised version.
Figure 3C: I would suggest removing the tracks and showing the expression levels in TPMs.
According to the reviewer’s suggestion, we have analyzed the results and showed the ISGs expression levels in fold change of TPMs (Figure 3D).
Figure 4C: It seems that the IP efficiency from METTL3 is lower in WTAP KO cells. That may impact the author's conclusions.
We have repeated the immunoprecipitation experiments of METTL3 and confirmed the immunoprecipitation (IP) efficiency from METTL3 had no difference between WTAP<sup>sgRNA</sup> cells and the control cells (Figure 5C).
I would suggest performing an IP of WTAP with the 5StoA mutation to confirm the missing interaction with WTAP.
According to the reviewer’s suggestion, we investigated the interaction between STAT1 and WTAP in WT cells and WTAP 5ST-A-rescued THP-1 cells. Our results showed that interaction between STAT1, METTL3 and WTAP were enhanced with WTAP 5ST-A mutation, which was depleted by hex treatment (Figure 5-figure supplement 1E). Thus, the interaction of WTAP WT or 5ST-A with the promoter regions of ISG were attenuated by WTAP LLPS dissolution (Figure 6E). Taken together, the interaction between STAT1 and MTC were relied on LLPS of WTAP.
In the graphical abstract, it is confusing to represent WTAP as a line. All other proteins are presented as circles. It is easy to confuse WTAP protein with an RNA. Additionally, m<sup>6</sup>A is too big in size. It should be smaller than a protein.
We thank the reviewer for raising this suggestion. We have modified the graphical abstract to avoid the confusion in our revised version (Figure 6F).
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(15) Zhan, Z., Cao, H., Xie, X., Yang, L., Zhang, P., Chen, Y., Fan, H., Liu, Z., and Liu, X. (2015). Phosphatase PP4 Negatively Regulates Type I IFN Production and Antiviral Innate Immunity by Dephosphorylating and Deactivating TBK1. J Immunol 195, 3849-3857. 10.4049/jimmunol.1403083.
(16) Raja, R., Wu, C., Bassoy, E.Y., Rubino, T.E., Jr., Utagawa, E.C., Magtibay, P.M., Butler, K.A., and Curtis, M. (2022). PP4 inhibition sensitizes ovarian cancer to NK cell-mediated cytotoxicity via STAT1 activation and inflammatory signaling. J Immunother Cancer 10. 10.1136/jitc-2022-005026.
(17) Rubio, R.M., Depledge, D.P., Bianco, C., Thompson, L., and Mohr, I. (2018). RNA m(6) A modification enzymes shape innate responses to DNA by regulating interferon beta. Genes Dev 32, 1472-1484. 10.1101/gad.319475.118.
(18) Ge, Y., Ling, T., Wang, Y., Jia, X., Xie, X., Chen, R., Chen, S., Yuan, S., and Xu, A. (2021). Degradation of WTAP blocks antiviral responses by reducing the m(6) A levels of IRF3 and IFNAR1 mRNA. EMBO Rep 22, e52101. 10.15252/embr.202052101.
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eLife Assessment
TDP-43 mislocalization is a key feature of some neurodegenerative diseases, but cellular models are lacking. The authors endogenously-tagged TDP-43 with a C-terminal GFP tag in human iPSCs, followed by expression of an intrabody-NES that targeted GFP to the cytosol. They convincingly report physical mislocalization and functional depletion of TDP-43, as measured by microscopy and RNAseq. This method will be valuable to investigators studying the biological consequences of TDP-43 mislocalization and the methodology is in line with the current state-of-the-art.
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Reviewer #2 (Public review):
Summary:
TDP-43 mislocalization occurs in nearly all of ALS, roughly half of FTD, and as a co-pathology in roughly half of AD cases. Both gain of function and loss of function mechanisms associated with this mislocalization likely contribute to disease pathogeneisis.
Here, the authors describe a new method to induce TDP-43 mislocalization in cellular models. They endogenously-tagged TDP-43 with a C-terminal GFP tag in human iPSCs. They then expressed an intrabody - fused with a nuclear export signal (NES) - that targeted GFP to the cytosol. Expression of this intrabody-NES in human iPSC derived neurons induced nuclear depletion of homozygous TDP-43-GFP, caused its mislocalization to the cytosol, and at least in some cells appeared to cause cytosolic aggregates. This mislocalization was accompanied by induction of cryptic exons in well characterized transcripts known to be regulated by TDP-43, a hallmark of functional TDP-43 loss and consistent with pathological nuclear TDP-43 depletion. Interestingly, in heterozygous TDP-43-GFP neurons, expression of intrabody-NES appeared to also induce the mislocalization of untagged TDP-43 in roughly half of the neurons, suggesting that this system can also be used to study effects on untagged endogenous TDP-43 as well as TDP-43-GFP fusion protein.
Strengths:
A clearer understanding of how TDP-43 mislocalization alters cellular function, as well as pathways that mitigate clearance of TDP-43 aggregates, is critical. But modeling TDP-43 mislocalization in disease-relevant cellular systems has proven to be challenging. High levels of overexpression of TDP-43 lacking an NES can drive endogenous TDP-43 mislocalization, but such overexpression has direct and artificial consequences on certain cellular features (e.g. altered exon skipping) not seen in diseased patients. Toxic small molecules such as MG132 and arsenite can induce TDP-43 mislocalization, but co-induce myriad additional cellular dysfunctions unrelated to TDP-43 or ALS. TDP-43 binding oligonucleotides can cause cytosolic mislocalization as well. Each system has pros and cons, and additional ways to induce TDP-43 mislocalization would be useful for the field. The method described in this manuscript could provide researchers with a powerful way to study the combined biology of cytosolic TDP-43 mislocalization and nuclear TDP-43 depletion, with additional temporal control that is lacking in current method. Indeed, the author see some evidence of differences in RNA splicing caused by pure TDP-43 depletion versus their induced mislocalization model. Finally, their method may be especially useful in determining how TDP-43 aggregates are cleared by cells, potentially revealing new biological pathways that could be therapeutically targeted.
Weaknesses:
The method and supporting data have some limitations.
• Tagging of TDP-43 with a bulky GFP tag may alter its normal physiological functions, for example, phase separation properties and functions within complex ribonucleoprotein complexes. The authors show that normal splicing function of GFP-TDP-43 is maintained, suggesting that physiology is largely preserved, but other functions and properties of TDP-43 that were not directly tested could be altered.
• Potential differences in splicing and micro RNAs between TDP-43 knockdown and TDP-43 mislocalization are potentially interesting. However, different patterns of dysregulated RNA splicing can occur at different levels of TDP-knockdown and can differ in different batches of experiments, thus it is difficult to asses whether the changes observed in this paper are due to mislocalization per se, or rather just reflect differences in nuclear TDP-43 abundance or batch effects.
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Author response:
The following is the authors’ response to the previous reviews
Public Reviews:
Reviewer #1 (Public Review):
Summary:
Nuclear depletion and cytoplasmic mislocalization/aggregation of the DNA and RNA binding protein TDP-43 are pathological hallmarks of multiple neurodegenerative diseases. Prior work has demonstrated that depletion of TDP-43 from the nucleus leads to alterations in transcription and splicing. Conversely, cytoplasmic mislocalization/aggregation can contribute to toxicity by impairing mRNA transport and translation as well as miRNA dysregulation. However, to date, models of TDP-43 proteinopathy rely on artificial knockdown- or overexpression-based systems to evaluate either nuclear loss or cytoplasmic gain of function events independently. Few model systems authentically reproduce both nuclear depletion and cytoplasmic miscloalization/aggregation events. In this manuscript, the authors generate novel iPSC-based reagents to manipulate the localization of endogenous TDP-43. This is a valuable resource for the field to study pathological consequences of TDP-43 proteinopathy in a more endogenous and authentic setting. However, in the current manuscript, there are a number of weaknesses that should be addressed to further validate the ability of this model to replicate human disease pathology and demonstrate utility for future studies.
Strengths:
The primary strength of this paper is the development of a novel in vitro tool.
Weaknesses:
There are a number of weaknesses detailed below that should be addressed to thoroughly validate these new reagents as more authentic models of TDP-43 proteinopathy and demonstrate their utility for future investigations.
(1) The authors should include images of their engineered TDP-43-GFP iPSC line to demonstrate TDP-43 localization without the addition of any nanobodies (perhaps immediately prior to addition of nanobodies). Additionally, it is unclear whether simply adding a GFP tag to endogenous TDP-43 impact its normal function (nuclear-cytoplasmic shuttling, regulation of transcription and splicing, mRNA transport etc).
We have included images of the untransduced day 20 MNs derived from the engineered TDP43-GFP iPSC lines and the unedited line (Supplementary Fig. 1B).
We acknowledge the reviewer’s concern about the potential impact of the GFP tag on TDP43's normal function. To address this, we have validated the functionality of TDP43 by assessing the inclusion of cryptic exons in highly sensitive targets such as UNC13A and STMN2, both of which are known to be directly regulated by TDP43.
We compared MNs derived from the unedited parent line with the TDP43-GFP MNs prior to nanobody addition. As measured by qPCR, cryptic exon inclusion in UNC13A and STMN2 was not observed in the unedited or edited TDP43-GFP MNs (Supplementary Fig.1C), confirming that the tagging does not induce splicing defects by itself. The cryptic exon inclusion in UNC13A and STMN2 were only observed in TDP43-GFP MNs expressing the NES nanobody (Supplementary Fig. 2D). These findings were further supported by our next-generation sequencing data, which also showed that cryptic exon inclusion was specific to the TDP43 mislocalization condition (Supplementary Fig.3 and 4).
Thus, we have strong evidence that the GFP-tagged TDP43 behaves similarly to the wild-type protein and does not interfere with its function in our model.
(2) Can the authors explain why there is a significant discrepancy in time points selected for nanobody transduction and immunostaining or cell lysis throughout Figure 1 and 2? This makes interpretation and overall assessment of the model challenging.
For the phenotypic data shown in Fig.1, we added the AAVs at day 18 or 20 and analyzed the cells at day 40. For the phosphorylated TDP43 western blot (revised Fig. 3D), cells were treated with doxycycline at day 20 to induce nanobody expression and samples were harvested at day 40. Thus, cells were harvested between days 20 or 22 after adding the nanobodies. The onset of transgene expression when using AAVs in neurons typically display slow kinetics. We observed TDP43 mislocalization in less than 50% of the neurons after 7 days post-transduction that peaked at 10-12 days after addition of the nanobodies, when more than 80% of the cells displayed TDP43 mislocalization. Hence, we do not believe that a two-day difference significantly alters the interpretation of the data.
The decision to harvest neurons at day 30 for the qPCR data was taken to investigate whether the splicing changes seen at day 40 from the transcriptomics analysis can be detected well before the phenotypes observed at day 40.
(3) The authors should further characterize their TDP-43 puncta. TDP-43 immunostaining is typically punctate so it is unclear if the puncta observed are physiologic or pathologic based on the analyses carried out in the current version of this manuscript. Additionally, do these puncta co-localize with stress granule markers or RNA transport granule markers? Are these puncta phosphorylated (which may be more reminiscent of end-stage pathologic observations in humans)?
We have tried immunostaining neurons for phosphorylated TDP43. However, our immunostaining attempts were unsuccessful. Depending on the antibody, we either saw no signal (antibody from Cosmo Bio, TIP-PTD-M01A) or even the control neurons displayed detectable phosphorylation within the nucleus (antibody from Proteintech 22309-1-AP). Consequently, we performed western blot analysis using an antibody from Cosmo Bio, (TIP-PTD-M01A) that clearly shows hyperphosphorylation of TDP43 in whole cell lysates (Fig. 3D, E). Hence, we have referred to these structures as puncta and not aggregates (Page 4).
To assess co-localization of the puncta with stress granules, we immunostained for the stress granule marker G3BP1. This was done in MNs that were treated with sodium arsenite (SA) or PBS as a control. In the PBS treated control MN cultures, TDP43 mislocalization alone did not induce stress granule formation. G3BP1+ stress granules were only observed following SA stress (0.5 mM, 60 minutes). Further, only a subset of TDP43 puncta overlapped with these stress granules (Supplementary Fig. 7) (Page 6).
(4) The authors should include multiple time points in their evaluation of TDP-43 loss of function events and aggregation. Does loss of function get worse over time? Is there a time course by which RNA misprocessing events emerge or does everything happen all at once? Does aggregation get worse over time? Do these neurons die at any point as a result of TDP-43 proteinopathy?
We agree that a time course to analyze TDP43 mislocalization and its consequences would be ideal. However, the mislocalization of TDP43 across neurons is not a coordinated process. At each given time instance, neurons display varying levels of TDP43 mislocalization. Answering the questions raised by the reviewer would require tracking individual neurons in real time in a controlled environment over weeks. Unfortunately, we currently do not have the hardware to run these experiments. However, we do observe increased levels of cleaved caspase 3 in MNs expressing the NES nanobody, indicating that these neurons indeed undergo apoptosis by day 40 (Fig.1).
We have, however, analyzed changes in splicing using qPCR for 12 genes over a time course starting as early as 4 hours after inducing mislocalization. We detect time-dependent cryptic splicing events in all genes as early as 8 hours after doxycycline addition, coinciding with the appearance TDP43 mislocalization (Fig. 4A, B).
(5) Can the authors please comment on whether or not their model is "tunable"? In real human disease, not every neuron displays complete nuclear depletion of TDP-43. Instead there is often a gradient of neurons with differing magnitudes of nuclear TDP-43 loss. Additionally, very few neurons (5-10%) harbor cytoplasmic TDP-43 aggregates at end-stage disease. These are all important considerations when developing a novel authentic and endogenous model of TDP-43 proteinopathy which the current manuscript fails to address.
As shown in Fig .1, the neurons expressing the NES-nanobody display a wide range of mislocalization as assessed by the % of nuclear TDP43 present. By titrating the amount of AAVs added to the culture, the model can be tuned to achieve a wide gradient of TDP43 mislocalization.
We calculated the size and percentage of neurons displaying TDP43 puncta. The size and the number of aggregates varies across the neurons that display TDP43 mislocalization. Around 50% of the neurons displayed small (1 um<sup>2</sup>) puncta while large puncta (> 5 um<sup>2</sup>) were observed in <10% of the cells, similar to observations in patient tissue (Fig. 1F).
Reviewer #2 (Public Review):
Summary:
TDP-43 mislocalization occurs in nearly all of ALS, roughly half of FTD, and as a co-pathology in roughly half of AD cases. Both gain-of-function and loss-of-function mechanisms associated with this mislocalization likely contribute to disease pathogeneisis.
Here, the authors describe a new method to induce TDP-43 mislocalization in cellular models. They endogenously tagged TDP-43 with a C-terminal GFP tag in human iPSCs. They then expressed an intrabody - fused with a nuclear export signal (NES) - that targeted GFP to the cytosol. Expression of this intrabody-NES in human iPSC-derived neurons induced nuclear depletion of homozygous TDP-43-GFP, caused its mislocalization to the cytosol, and at least in some cells appeared to cause cytosolic aggregates. This mislocalization was accompanied by induction of cryptic exons in well characterized transcripts known to be regulated by TDP-43, a hallmark of functional TDP-43 loss and consistent with pathological nuclear TDP-43 depletion. Interestingly, in heterozygous TDP-43-GFP neurons, expression of intrabody-NES appeared to also induce the mislocalization of untagged TDP-43 in roughly half of the neurons, suggesting that this system can also be used to study effects on untagged endogenous TDP-43 as well as TDP-43-GFP fusion protein.
Strengths:
A clearer understanding of how TDP-43 mislocalization alters cellular function, as well as pathways that mitigate clearance of TDP-43 aggregates, is critical. But modeling TDP-43 mislocalization in disease-relevant cellular systems has proven to be challenging. High levels of overexpression of TDP-43 lacking an NES can drive endogenous TDP-43 mislocalization, but such overexpression has direct and artificial consequences on certain cellular features (e.g. altered exon skipping) not seen in diseased patients. Toxic small molecules such as MG132 and arsenite can induce TDP-43 mislocalization, but co-induce myriad additional cellular dysfunctions unrelated to TDP-43 or ALS. TDP-43 binding oligonucleotides can cause cytosolic mislocalization as well. Each system has pros and cons, and additional ways to induce TDP-43 mislocalization would be useful for the field. The method described in this manuscript could provide researchers with a powerful way to study the combined biology of cytosolic TDP-43 mislocalization and nuclear TDP-43 depletion, with additional temporal control that is lacking in current method. Indeed, the authors see some evidence of differences in RNA splicing caused by pure TDP-43 depletion versus their induced mislocalization model. Finally, their method may be especially useful in determining how TDP-43 aggregates are cleared by cells, potentially revealing new biological pathways that could be therapeutically targeted.
Weaknesses:
The method and supporting data have limitations in its current form, outlined below, and in its current form the findings are rather preliminary.
(1) Tagging of TDP-43 with a bulky GFP tag may alter its normal physiological functions, for example phase separation properties and functions within complex ribonucleoprotein complexes. In addition, alternative isoforms of TDP-43 (e.g. "short" TDP-43, would not be GFP tagged and therefore these species would not be directly manipulatable or visualizable with the tools currently employed in the manuscript.
With reference to our answer above, we have confirmed using qPCR and RNA-seq analysis that adding a GFP tag to the C-terminus of TDP43 does not result in an appreciable loss of functionality. We do not observe any cryptic exon inclusion in STMN2 and UNC13A. Cryptic exon inclusion in these genes, especially STMN2, has been recognized as a very sensitive indicator of TDP43 loss of function (Supplementary Fig 1C, Supplementary 2D, Fig. 3, Fig.4)
We acknowledge that truncated alternatively spliced versions of TDP43 will lose the GFP-tag and cannot be manipulated with our system. Since our GFP tag is positioned on the C-terminus, our system cannot manipulate these truncated fragments as the tag is lost in these isoforms. But these isoforms, if present, should be detectable using the Proteintech antibody against total TDP43, which recognizes N-terminal TDP43 epitopes. However, western blot analysis, even 20 days after inducing TDP43 mislocalization, showed no truncated fragments. This suggests that TDP43 mislocalization alone is insufficient to generate significant levels of truncated isoforms. We have added this section to the Limitations paragraph (page 9).
(2) The data regarding potential mislocalization of endogenous TDP-43 in the heterozygous TDP-43-GFP lines is especially intriguing and important, yet very little characterization was done. Does untagged TDP-43 co-aggregate with the tagged TDP-43? Is localization of TDP-43 immunostaining the same as the GFP signal in these cells?
The purpose of the heterozygous experiments was to see whether mislocalized TDP43 could potentially trap the untagged TDP43. If this was not the case, we would have seen a maximum of 50% of the TDP43 signal mislocalized to the cytoplasm. The fact that a sizeable proportion of cells had significantly higher levels of TDP43 loss from the nucleus, indicates that mislocalized TDP43 can indeed trap the untagged protein fraction. We used GFP immunostaining to identify the tagged TDP43 while an antibody against the endogenous TDP43 protein was used to detect total TDP43 levels. In the cells that show near complete loss of nuclear TDP43, the total TDP43 signal coincides with the GFP (tagged TDP43) signal. We are unable to distinguish the untagged fraction selectively as we do not have an antibody that can detect this directly.
But we agree with the reviewer that these observations need further detailed follow-up that we are unable to provide currently. Hence, we have removed this figure from the manuscript.
(3) The experiments in which dox was used to induce the nanobody-NES, then dox withdrawn to study potential longer-lasting or self-perpetuating inductions of aggregation is potentially interesting. However, the nanobody was only measured at the RNA level. We know that protein half lives can be very long in neurons, and therefore residual nanobody could be present at these delayed time points. The key measurement to make would be at the protein level of the nanobody if any conclusions are be made from this experiment.
The reviewer has highlighted an important point. To address this issue, we tagged the nanobodies with a V5 tag that allowed us to directly measure nanobody levels within cells. After Dox withdrawal, we indeed observed significant expression of the nanobody within cells even after two weeks of Dox withdrawal. Extending the time point to three weeks allowed complete loss of the nanobody in most neurons. However, in contrast to our observations at two weeks, this was accompanied by a reversal of TDP43 mislocalization in these neurons at three weeks (Fig. 5).
Surprisingly, in less than 10% of the neurons, we observed >80% of the total TDP43 still mislocalized to the cytoplasm, despite nearly undetectable levels of the nanobody. Super-resolution microscopy further revealed persistent cytoplasmic TDP43 in these neurons that did not overlap with residual nanobody signal. This suggests that in these neurons, the nanobody was no longer required to maintain TDP43 mislocalization (Fig. 5, page 7)
(4) Potential differences in splicing and microRNAs between TDP-43 knockdown and TDP-43 mislocalization are potentially interesting. However, different patterns of dysregulated RNA splicing can occur at different levels of TDP-knockdown, thus it is difficult to assess whether the changes observed in this paper are due to mislocalization per se, or rather just reflect differences in nuclear TDP-43 abundance.
This a fair point. It is possible that microRNA dysregulation might require a greater loss of nuclear TDP43 and maybe more resilient to TDP43 loss as compared to splicing. We have acknowledged this in the discussion section (page 9).
Recommendations for the authors:
Reviewer #1 (Recommendations For The Authors):
(1) It would be helpful to include nuclear vs cytoplasmic ratios of TDP-43 instead of simply "% nuclear TDP-43"
We have used % nuclear TDP43 as these values have biologically meaningful upper and lower bounds, which makes it easier to compare across experiments. We found that using a ratio of nuclear vs cytoplasmic TDP43 intensities displayed higher variability and a wider range.
We have re-labelled the y-axis as “% Nuclear TD43 / soma TDP43” to make our quantification clearer. The conversion from % nuclear TDP43 to N/C is straightforward. If the % nuclear TDP43 is X, then the N/C ratio can be calculated as X / (100-X). For example, a % nuclear TDP43 of 80% would amount to an N/C ratio of 80/20 = 4.
(2) The axis descriptions in Figure 1D are very unclear. While this is described better in the figure legend, it would be beneficial to have a more descriptive y-axis title in the figure (which may mean increasing the number of graphs).
Axis descriptions and figures changed as recommended.
(3) In Figure 1, the time points at which iPSNs were transduced with nanobody and/or fixed for immunostaining is somewhat inconsistent across all panels. This hinders interpretation of the figure as a whole. The authors should use same transduction and immunostaining time points for consistency or demonstrate that the same phenotype is observed regardless of transduction and immunostaining day as long as the time in between (time of nano body expression) is consistent. Subsequently, in Figure 2, a different set of time points is used.
Please see our response in the public comments above
(4) In Figure 1, please show individual data points for each independent differentiation to demonstrate the level of reproducibility from batch to batch.
Data points have been shown per replicate (Supplementary Fig. 2)
We have refined our approach for phenotypic analysis to improve consistency across different clones. Previously, we set thresholds on % nuclear TDP43 to distinguish MNs with nuclear versus mislocalized TDP43. This was done by ranking all cells based on % nuclear TDP43 and applying quantile-based thresholds—designating the top 25% as control and the bottom 25% as mislocalized, ensuring equal number of cells per category. However, we observed significant variability in thresholds across clones. For instance, the E8 clone had thresholds of 96% and 29%, while the E5 clone had 93% and 40%.
To address this, we reanalysed the data using a standardized three-bin approach:
(1) Control: MNs expressing the control nanobody.
(2) Low-Moderate Mislocalization: MNs expressing the NES nanobody with > 40% nuclear TDP43.
(3) Severe Mislocalization: MNs expressing the NES nanobody with < 40% nuclear TDP43.
This approach ensured a more reliable comparison of TDP43 mislocalization effects across experiments. The conclusions remain the same.
(5) In Figure 2, please show individual data points.
Data points for all the qPCR analyses in the paper have been included as a supplementary text file.
(6) In Figure 3, please show individual data points.
Data points for the western blot data have been included as a supplementary data file.
All other comments are within the public review.
Reviewer #2 (Recommendations For The Authors):
(1) In general more robust quantification of many of the described phenotypes are necessary. In particular, no apparent quantification of cytosolic mislocalization was performed in Figure 1, or quantification of mislocalization of Figure 3F. It is unclear in the western blot in Fig 1G if TDP-43 signal were normalized to total protein, and of note it seems that expression of the intrabody-NES reduced total proteins in the western blots that were shown. No quantification or measurement of the insoluble material was done or shown.
We have quantified cytosolic mislocalization of TDP43 (Fig. 1C). The y-axis indicates the total TDP43 signal observed in the nucleus as a percentage of the total signal observed in the soma (including the nucleus). This value has the advantage of ranging between 100% (perfectly nuclear) to 0% (complete nuclear loss). The boxplots indicate that expression of the NES-nanobody results in a range of cytosolic mislocalization with a median value around 40% of the TDP43 remaining in the nucleus.
Western blot data in previous Fig. 1G was normalized to alpha-tubulin. We were unable to get a good signal for the insoluble fraction. From the alpha-tubulin alone, it cannot be concluded that NES-nanobody results in a decrease in total protein levels. In the revised western blot for phosphorylated TDP43 (Fig. 3D, E), we have quantified total and phosphorylated TDP43. Here, we observe a six-fold increase in the levels of phosphorylated TDP43 without a significant change in total TDP43 protein levels.
To avoid potential mis-interpretation of our results, we have now removed the previous Fig. 1G.
(2) Additional images of nearly all microscopy data at higher magnifications would be required to better evaluate TDP-43 localization. Ideally including images for each channel in addition to merged images, and especially for key figures such as Figure 1B, 3B, 3F.
Better images have been provided.
(3) No control images were shown for Figure 1F and 3F. It is unclear what the bright punctate spots of cytoplasmic TDP-43 GFP signal represent. Are these true aggregates? If so, additional characterization would be required before such conclusions can be made, beyond the relatively superficial western blot analysis that was done in Figure 1.
Control images have now been provided (Figure 1E). As we mentioned above, immunostaining analysis to characterize whether the aggregates are phosphorylated failed to provide a clear signal. However, we have now confirmed that the mislocalized TDP43 is indeed hyper-phosphorylated (Figure 3D, E). We have acknowledged this in the main text, and have referred to these as puncta reminiscent of aggregates (Page 4, Page 6).
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Author response:
The following is the authors’ response to the original reviews
Public Reviews:
Reviewer #1 (Public review):
Summary:
The authors set out to explore the role of upstream open reading frames (uORFs) in stabilizing protein levels during Drosophila development and evolution. By utilizing a modified ICIER model for ribosome translation simulations and conducting experimental validations in Drosophila species, the study investigates how uORFs buffer translational variability of downstream coding sequences. The findings reveal that uORFs significantly reduce translational variability, which contributes to gene expression stability across different biological contexts and evolutionary timeframes.
We thank the reviewer for carefully reading our manuscript and providing thoughtful and constructive feedback. We believe the manuscript has been significantly improved by incorporating your suggestions. Please find our detailed responses and corresponding revisions below.
Strengths:
(1) The study introduces a sophisticated adaptation of the ICIER model, enabling detailed simulation of ribosomal traffic and its implications for translation efficiency.
(2) The integration of computational predictions with empirical data through knockout experiments and translatome analysis in Drosophila provides a compelling validation of the model's predictions.
(3) By demonstrating the evolutionary conservation of uORFs' buffering effects, the study provides insights that are likely applicable to a wide range of eukaryotes.
We appreciate your positive feedback and thoughtful summary of the strengths of our study.
Weaknesses:
(1) Although the study is technically sound, it does not clearly articulate the mechanisms through which uORFs buffer translational variability. A clearer hypothesis detailing the potential molecular interactions or regulatory pathways by which uORFs influence translational stability would enhance the comprehension and impact of the findings.
Thanks for your constructive comments. In the Discussion section of our previous submission (Original Lines 470-489), we proposed that uORFs function as “molecular dams” to smooth out fluctuations in ribosomal flow toward downstream CDS regions, primarily via mechanisms involving ribosome collision and dissociation. To further address your concern, we have expanded the Discussion and included a new model figure (Fig. 9) to more clearly articulate the potential biological and mechanistic basis by which translating 80S ribosomes may induce the dissociation of 40S ribosomes. The revised section (Lines 540–557) now reads:
“Ribosome slowdown or stalling on mRNA due to rare codons [56,96-98] or nascent blocking peptides [99-102] frequently triggers ribosome collisions genome-wide [103-105]. Such collisions, especially among elongating 80S ribosomes, often activate ribosome quality control (RQC) pathways that recognize collision interfaces on the 40S subunit, leading to ribosomal subunit dissociation and degradation [106-108]. In mammals, ZNF598 specifically identifies collided ribosomes to initiate ubiquitin-dependent protein and mRNA quality control pathways [109-113]. Analogously, yeast employs Hel2-mediated ubiquitination of uS10, initiating dissociation via the RQC-trigger complex (RQT) [114]. Furthermore, the human RQT (hRQT) complex recognizes ubiquitinated ribosomes and induces subunit dissociation similarly to yeast RQT [115]. However, transient ribosome collisions can evade RQC by promoting resumed elongation through mechanical force provided by trailing ribosomes, thereby mitigating stalling [116]. Beyond 80S collisions, evidence increasingly highlights a distinct collision type involving scanning 40S subunits or pre-initiation (43S) complexes. Recently, an initiation RQC pathway (iRQC) targeting the small ribosomal subunit (40S) has been described, particularly involving collisions between scanning 43S complexes or between stalled 43S and elongating 80S ribosomes (Figure 9B) [117,118]. During iRQC, E3 ubiquitin ligase RNF10 ubiquitinates uS3 and uS5 proteins, resulting in 40S degradation [118]. This mechanism aligns closely with our ICIER model, proposing collision-driven 43S dissociation in the 5' UTRs. Future studies exploring these mechanisms in greater detail will clarify how uORFs modulate translational regulation through buffering effects.”
(2) The study could be further improved by a discussion regarding the evolutionary selection of uORFs. Specifically, it would be beneficial to explore whether uORFs are favored evolutionarily primarily for their role in reducing translation efficiency or for their capability to stabilize translation variability. Such a discussion would provide deeper insights into the evolutionary dynamics and functional significance of uORFs in genetic regulation.
Thank you for this insightful suggestion. We agree that understanding whether uORFs are evolutionarily favored for their role in translational repression or for their capacity to buffer translational variability is a compelling and unresolved question. Our study suggests that translational buffering, rather than translational repression alone, can also drive evolutionary selection favoring uORFs, although it remains challenging to empirically disentangle these functions due to their inherent linkage. We have expanded the discussion in the revised manuscript to address this point in more detail (Lines 494-513), which is reproduced as follows:
“Previous studies have shown that a significant fraction of fixed uORFs in the populations of D. melanogaster and humans were driven by positive Darwinian selection 63,67, suggesting active maintenance through adaptive evolution rather than purely neutral or deleterious processes. While uORFs have traditionally been recognized for their capacity to attenuate translation of downstream CDSs, accumulating evidence now underscores their critical role in stabilizing gene expression under fluctuating cellular and environmental conditions [43,55,56]. Whether the favored evolutionary selection of uORFs acts primarily through their role in translational repression or translational buffering remains a compelling yet unresolved question, as these two functions are inherently linked. Indeed, highly conserved uORFs tend to be translated at higher levels, resulting not only in stronger inhibition of CDS translation [34,45,67] but also in a more pronounced buffering effect, as demonstrated in this study. This buffering capacity of uORFs potentially provides selective advantages by reducing fluctuations in protein synthesis, thus minimizing gene-expression noise and enhancing cellular homeostasis. This suggests that selection may favor uORFs that contribute to translational robustness, a hypothesis supported by findings in yeast and mammals showing that uORFs are significantly enriched in stressresponse genes and control the translation of certain master regulators of stress responses [41,42,94,95]. Our study suggests that translational buffering, rather than translational repression alone, can also drive evolutionary selection favoring uORFs, although it remains challenging to empirically disentangle these functions. Future comparative genomic analyses, coupled with experimental approaches such as ribosome profiling and functional mutagenesis, will be crucial in elucidating the precise evolutionary forces driving uORF conservation and adaptation.”
Reviewer #2 (Public review):
uORFs, short open reading frames located in the 5' UTR, are pervasive in genomes. However, their roles in maintaining protein abundance are not clear. In this study, the authors propose that uORFs act as "molecular dam", limiting the fluctuation of the translation of downstream coding sequences. First, they performed in silico simulations using an improved ICIER model, and demonstrated that uORF translation reduces CDS translational variability, with buffering capacity increasing in proportion to uORF efficiency, length, and number. Next, they analzed the translatome between two related Drosophila species, revealing that genes with uORFs exhibit smaller fluctuations in translation between the two species and across different developmental stages within the same specify. Moreover, they identified that bicoid, a critical gene for Drosophila development, contains a uORF with substantial changes in translation efficiency. Deleting this uORF in Drosophila melanogaster significantly affected its gene expression, hatching rates, and survival under stress condition. Lastly, by leveraging public Ribo-seq data, the authors showed that the buffering effect of uORFs is also evident between primates and within human populations. Collectively, the study advances our understanding of how uORFs regulate the translation of downstream coding sequences at the genome-wide scale, as well as during development and evolution.
The conclusions of this paper are mostly well supported by data, but some definitions and data analysis need to be clarified and extended.
We thank the reviewer for the thoughtful and constructive review. Your summary accurately captures the key findings of our study. We have carefully addressed all your concerns in the revised manuscript, and we believe it has been significantly improved based on your valuable input.
(1) There are two definitions of translation efficiency (TE) in the manuscript: one refers to the number of 80S ribosomes that complete translation at the stop codon of a CDS within a given time interval, while the other is calculated based on Ribo-seq and mRNA-seq data (as described on Page 7, line 209). To avoid potential misunderstandings, please use distinct terms to differentiate these two definitions.
Thank you for highlighting this important point, and we apologize for the confusion. The two definitions of translation efficiency (TE) in our manuscript arise from methodological differences between simulation and experimental analyses. To clarify, in the revised manuscript, we use “translation rate” in the context of simulations to describe the number of 80S ribosomes completing translation at the CDS stop codon per unit time. We retain the conventional “translation efficiency (TE)” for Ribo-seq–based measurements.
In this revised manuscript, we have added a more detailed explanation of TE in the revised manuscript (Lines 202–206), which now reads:
“For each sample, we followed established procedures [62-66] to calculate the translational efficiency (TE) for each feature (CDS or uORF). TE serves as a proxy for the translation rate at which ribosomes translate mRNA into proteins, typically quantified by comparing the density of ribosome-protected mRNA fragment (RPF) to the mRNA abundance for that feature (see Materials and Methods).”
(2) Page 7, line 209: "The translational efficiencies (TEs) of the conserved uORFs were highly correlated between the two species across all developmental stages and tissues examined, with Spearman correlation coefficients ranging from 0.478 to 0.573 (Fig. 2A)." However, the authors did not analyze the correlation of translation efficiency of conserved CDSs between the two species, and compare this correlation to the correlation between the TEs of CDSs. These analyzes will further support the authors conclusion regarding the role of conserved uORFs in translation regulation.
In the revised manuscript, we have incorporated a comparison of translational efficiency (TE) correlations for conserved CDSs between the two species. We found that CDSs exhibit significantly higher interspecific TE correlations than uORFs, with Spearman’s rho ranging from 0.588 to 0.806. This suggests that uORFs tend to show greater variability in TE than CDSs, consistent with our model in which uORFs buffer fluctuations in downstream CDS translation. The updated results were included in the revised manuscript (Lines 223-227) as follows:
“In contrast, TE of CDSs exhibited a significantly higher correlation between the two species in the corresponding samples compared to that of uORFs, with Spearman’s rho ranging from 0.588 to 0.806 (P = 0.002, Wilcoxon signed-rank test; Figure 2A). This observation is consistent with our simulation results, which indicate that uORFs experience greater translational fluctuations than their downstream CDSs.”
(3) Page 8, line 217: "Among genes with multiple uORFs, one uORF generally emerged as dominant, displaying a higher TE than the others within the same gene (Fig. 2C)." The basis for determining dominance among uORFs is not explained and this lack of clarification undermines the interpretation of these findings.
Thank you for pointing this out. We apologize for the confusion. In our study, a “dominant” uORF is defined as the one with the highest translation efficiency (TE) among all uORFs within the same gene. This designation is based solely on TE, which we consider a key metric for uORF activity, as it directly reflects translational output and potential regulatory impact. We have revised the manuscript to clarify this definition (Lines 232–244), now stating:
“Among genes with multiple uORFs, we defined the uORF with the highest TE as the dominant uORF for that gene, as TE is one of the most relevant metrics for assessing uORF function 45,67…… These results suggest that genes with multiple uORFs tend to retain the same dominant uORF across developmental stages, indicating that the dominant uORFs may serve as the key translational regulator of the downstream CDS.”
(4) According to the simulation, the translation of uORFs should exhibit greater variability than that of CDSs. However, the authors observed significantly fewer uORFs with significant TE changes compared to CDSs. This discrepancy may be due to lower sequencing depth resulting in fewer reads mapped to uORFs. Therefore, the authors may compare this variability specifically among highly expressed genes.
Thank you for this thoughtful observation. We agree that the lower proportion of uORFs showing significant TE changes compared to CDSs, as reported in Table 1, appears inconsistent with our conclusion that uORFs exhibit greater translational variability. However, this discrepancy is largely attributable to differences in sequencing depth and feature length—uORFs are generally much shorter and more weakly expressed than CDSs, resulting in fewer mapped reads and reduced statistical power (Figure S18A).
To address this issue, we first followed your suggestion and restricted our analysis to genes with both mRNA and RPF RPKM values above the 50th percentile in D. melanogaster and D. simulans. While this filtering increased the total proportion of features with significant TE changes (due to improved read coverage), the proportion of significant uORFs still remained lower than that of CDSs (Table R1). This suggests that even among highly expressed genes, the disparity in read counts between uORFs and CDSs persists (Figure S18B), and thus the issue is not fully resolved.
To better capture biological relevance, we compared the absolute values of log2(TE changes) between D. melanogaster and D. simulans for uORFs and their corresponding CDSs. Across all samples, uORFs consistently exhibit larger TE shifts than their downstream CDSs, supporting our model that uORFs act as translational buffers (Figure 3B).
We have made relevant changes to report the new analysis in this revised manuscript. Specifically, in our original submission, we stated this observation with the sentence “The smaller number of uORFs showing significant TE changes compared to CDSs between D. melanogaster and D. simulans likely reflects their shorter length and reduced statistical power, rather than indicating that uORFs are less variable in translation than CDSs.” To make this point clearer, in the revised version (Lines 275-284), we rephrased this sentence which read as follows:
“Note that due to their shorter length and generally lower TE, uORFs had considerably lower read counts than CDSs, limiting the statistical power to detect significant interspecific TE differences for uORFs. This trend consistently holds whether analyzing all expressed uORFs (Figure S18A) or only highly expressed genes (Figure S18B). Thus, the fewer uORFs showing significant TE divergence likely reflects lower read counts and statistical sensitivity rather than reduced translational variability relative to CDSs. In fact, the absolute values of log2(fold change) of TE for uORFs between D. melanogaster and D. simulans were significantly greater than those observed for corresponding CDSs across all samples (P < 0.001, Wilcoxon signed-rank test; Figure 3B), suggesting that the magnitude of
TE changes in CDSs is generally smaller than that in uORFs, due to the buffering effect of uORF.”
Author response table 1.
Proportion of uORFs and CDSs with significant TE changes before and after selecting HEGs
(5) If possible, the author may need to use antibodies against bicoid to test the effect of ATG deletion on bicoid expression, particularly under different developmental stages or growth conditions.
According to the authors' conclusions, the deletion mutant should exhibit greater variability in bicoid protein abundance. This experiment could provide strong support for the proposed mechanisms.
Thank you for this excellent suggestion. We fully agree that testing Bcd protein levels across developmental stages or stress conditions using antibodies would be a strong validation of our model, which predicts greater variability in Bcd protein abundance upon uORF deletion.
In fact, we attempted such experiments in both wild-type and mutant backgrounds. However, we encountered substantial difficulties in obtaining a reliable anti-Bcd antibody. Some Bcd antibodies referenced in the published literature were homemade and often shared among research groups as gifts [1-3] and some commercially available antibodies cited in previous studies are no longer supplied by vendors [4-6]. We managed to obtain a custom-made antibody from Professor Feng Liu, but unfortunately, it produced inconsistent and unsatisfactory results. Despite considerable effort—including during the COVID-19 pandemic—we were unable to identify a reagent suitable for robust and reproducible detection of Bcd protein.
As an alternative, we used sucrose gradient fractionation followed by qPCR to directly measure the translation efficiency of bicoid in vivo. We believe this approach offers a clear and quantitative readout of translational activity, and it avoids potential confounding from protein degradation, which may vary across conditions and developmental stages. Nonetheless, we recognize the value of antibody-based validation and will pursue this direction in future work if reliable antibodies become available. We have added this limitation to the revised Discussion section (Lines 563–568) as follows:
“We demonstrated that the bcd uORF represses CDS translation using sucrose gradient fractionation followed by qPCR—an approach that directly measures translation efficiency while minimizing confounding from RNA/protein degradation. However, detecting Bcd protein levels with antibodies across developmental stages or conditions in the mutants and wild-type controls would provide an even stronger validation of our model and should be explored in future studies.”
Recommendations for the authors:
Reviewer #1 (Recommendations for the authors):
(1) The authors should provide a more detailed explanation for the modifications made to the ICIER model. Specifically, an explanation of the biological or mechanistic rationale behind the ability of the 80S ribosome to cause upstream 40S ribosomes to dissociate from mRNA would help clarify this aspect of the model.
Thank you for this suggestion. In the original submission, we described our modifications to the ICIER model in the section titled “An extended ICIER model for quantifying uORF buffering in CDS translation” (Lines 88-124 of the revised manuscript).
To further clarify the biological rationale behind this mechanism, we have now included a conceptual model figure (Figure 9) illustrating mechanistically how uORF translation can buffer downstream translation within a single mRNA molecule. Additionally, we expanded the Discussion to summarize the current understanding of how collisions between translating 80S ribosomes and scanning 40S subunits may lead to dissociation, referencing known initial ribosome quality control (iRQC) pathways. These revisions provide a clearer mechanistic framework for interpreting the buffering effects modeled in our simulations. The relevant part is reproduced from Discussion (Lines 540-557) which reads as follows:
“Ribosome slowdown or stalling on mRNA due to rare codons [56,96-98] or nascent blocking peptides [99-102] frequently triggers ribosome collisions genome-wide [103-105]. Such collisions, especially among elongating 80S ribosomes, often activate ribosome quality control (RQC) pathways that recognize collision interfaces on the 40S subunit, leading to ribosomal subunit dissociation and degradation [106-108]. In mammals, ZNF598 specifically identifies collided ribosomes to initiate ubiquitin-dependent protein and mRNA quality control pathways [109-113]. Analogously, yeast employs Hel2-mediated ubiquitination of uS10, initiating dissociation via the RQC-trigger complex (RQT) [114]. Furthermore, the human RQT (hRQT) complex recognizes ubiquitinated ribosomes and induces subunit dissociation similarly to yeast RQT [115]. However, transient ribosome collisions can evade RQC by promoting resumed elongation through mechanical force provided by trailing ribosomes, thereby mitigating stalling [116]. Beyond 80S collisions, evidence increasingly highlights a distinct collision type involving scanning 40S subunits or pre-initiation (43S) complexes. Recently, an initiation RQC pathway (iRQC) targeting the small ribosomal subunit (40S) has been described, particularly involving collisions between scanning 43S complexes or between stalled 43S and elongating 80S ribosomes (Figure 9B) [117,118]. During iRQC, E3 ubiquitin ligase RNF10 ubiquitinates uS3 and uS5 proteins, resulting in 40S degradation [118]. This mechanism aligns closely with our ICIER model, proposing collision-driven 43S dissociation in the 5' UTRs. Future studies exploring these mechanisms in greater detail will clarify how uORFs modulate translational regulation through buffering effects.”
(2) The figure legend references Figure 5C; however, this figure appears to be missing from the document.
We apologize for the oversight. The missing panel previously referred to as Figure 5C has now been incorporated into the revised Figure 6A. The figure and its corresponding legend have been corrected accordingly in the updated manuscript.
Reviewer #2 (Recommendations for the authors):
This is an important study that enhances our understanding of the roles of uORFs in translational regulation. In addition to the suggestions provided in the public review, the following minor points should be addressed before publication in eLife:
(1) Page 7, line 207: "We identified 18,412 canonical uORFs shared between the two species (referred to as conserved uORFs hereafter)." The term "canonical uORFs" requires clarification. Does this refer to uORFs with specific sequence features, conservation, or another defining characteristic?
Thank you for pointing this out. We apologize for the lack of clarity. In our study, a canonical uORF is defined as an open reading frame (ORF) that initiates with a canonical AUG start codon located in the 5′ untranslated region (UTR) and terminates with a stop codon (UAA, UAG, or UGA) within the same mRNA. Conservation of uORFs is defined solely based on the presence of AUG start codons at orthologous positions in the 5′ UTR across species, regardless of differences in the stop codon.
To clarify this definition, we have revised the sentence as follows (Lines 213-219): “We focused on canonical uORFs that initiate with an ATG start codon in the 5′ UTR and terminate with a stop codon (TAA, TAG, or TGA). Because the ATG start codon is the defining feature of a canonical uORF and tends to be more conserved than its downstream sequence [67], we defined uORF conservation based on the presence of the ATG start codon in the 5′ UTR of D. melanogaster and its orthologous positions in D. simulans, regardless of differences in the stop codon. Using this criterion, we identified 18,412 canonical uORFs with conserved start codons between the two species.”
(2) Page 8, line 227: "Furthermore, the dominant uORFs showed a higher proportion of conserved uATGs than the other translated uORFs." There appears to be a typographical error. Should "other uATGs" instead read "other uORFs"?
Thank you for pointing this out. As we addressed in response to your previous concern, in this study, we defined uORF conservation primarily based on the presence of their start codon (uATG) both in D. melanogaster and the orthologous sites of D. simulans, as the start codon is the defining feature of a uORF and tends to be more conserved than the remaining sequence, as demonstrated in our previous study [7]. We used the term “conserved uATGs” to reflect this definition and believe it accurately conveys the intended meaning in this context.
(3) Page 8, line 240: "uORFs exhibited a significant positive correlation with the TE of their downstream CDSs in all samples analyzed (P < 0.001, Spearman's correlation)." A Spearman's rho of 0.11 or 0.21 may not practically represent a "significant" positive correlation. Consider rephrasing this as "a positive correlation."
Thank you for the suggestion. We have revised the sentence in the manuscript to read (Lines 257-259): “uORFs exhibited a modest, yet statistically significant, positive correlation with the TE of their downstream CDSs across all samples analyzed (P < 0.001, Spearman’s correlation).”
(4) Page 9, line 269: The analysis of interspecific TE changes between uORFs and their corresponding CDSs is a crucial piece of evidence supporting the authors' conclusions. Presenting this analysis as part of the figures, rather than in "Table 1," would improve clarity and accessibility.
Thank you for this suggestion. In Table 1, we originally presented the number of uORFs and CDSs that showed significant differences in TE between D. melanogaster and D. simulans during various developmental stages. One key point we aimed to emphasize was that, although TE changes in uORFs and their downstream CDSs are positively correlated, there is a notable difference in the magnitude of these changes. To better convey this, we have summarized the core findings of Table 1 in graphical form.
In Figure 3B of the revised version, we compared the absolute values of interspecific TE changes between CDS and uORF, showing that CDSs consistently exhibit smaller shifts than their upstream uORFs. This result further supports the translational buffering effect of uORFs on downstream CDS expression. We have included the updated results in the revised manuscript (Lines 281-284) as follows:
“In fact, the absolute values of log2(fold change) of TE for uORFs between D. melanogaster and D. simulans was significantly greater than that observed for corresponding CDSs across all samples (P < 0.001, Wilcoxon signed-rank test; Figure 3B), suggesting that the magnitude of TE changes in CDSs is generally smaller than that in uORFs, due to the buffering effect of uORF.”
(5) Page 9, line 279: The phrase "dominantly translated" needs clarification. Does it refer to Figure 2C, where one uORF is dominantly translated within a gene, or does it mean that the uORF's translation is higher than that of its corresponding CDS?
We apologize for the obscurity. The phrase "dominantly translated" means one uORF with the highest TE compared to other uORFs within a gene. We have rephrased the relevant sentence in the revised version (Lines 299-304), which now reads:
“To investigate how the conservation level and translation patterns of uORFs influence their buffering capacity on CDS translation, we categorized genes expressed in each pair of samples into three classes:
Class I, genes with conserved uORFs that are dominantly translated (i.e., exhibiting the highest TE among all uORFs within the same gene) in both Drosophila species; Class II, genes with conserved uORFs that are translated in both species but not dominantly translated in at least one; and Class III, the remaining expressed genes.”
(6) The sequencing data and analysis code should be made publicly available before publication to ensure transparency and reproducibility.
Thank you for this suggestion. As described in the Data availability section, all deepsequencing data generated in this study, including single-ended mRNA-Seq and Ribo-Seq data of 10 developmental stages and tissues of Drosophila simulans and paired-end mRNA-Seq data of 0-2 h, 26 h, 6-12 h, and 12-24 h Drosophila melanogaster embryos, were deposited in the China National Genomics Data Center Genome Sequence Archive (GSA) under accession numbers CRA003198, CRA007425, and CRA007426. The mRNA-Seq and Ribo-Seq data for the different developmental stages and tissues of Drosophila melanogaster were published in our previous paper [8] and were deposited in the Sequence Read Archive (SRA) under accession number SRP067542.
All original code has been deposited on GitHub: https://github.com/lujlab/uORF_buffer; https://github.com/lujlab/Buffer_eLife2025.
Response reference
(1) Li, X.Y., MacArthur, S., Bourgon, R., Nix, D., Pollard, D.A., Iyer, V.N., Hechmer, A., Simirenko, L., Stapleton, M., Luengo Hendriks, C.L., et al. (2008). Transcription factors bind thousands of active and inactive regions in the Drosophila blastoderm. PLoS Biol 6, e27. 10.1371/journal.pbio.0060027.
(2) Horner, V.L., Czank, A., Jang, J.K., Singh, N., Williams, B.C., Puro, J., Kubli, E., Hanes, S.D., McKim, K.S., Wolfner, M.F., and Goldberg, M.L. (2006). The Drosophila calcipressin sarah is required for several aspects of egg activation. Curr Biol 16, 1441-1446. 10.1016/j.cub.2006.06.024.
(3) Lee, K.M., Linskens, A.M., and Doe, C.Q. (2022). Hunchback activates Bicoid in Pair1 neurons to regulate synapse number and locomotor circuit function. Curr Biol 32, 2430-2441 e2433. 10.1016/j.cub.2022.04.025.
(4) Wharton, T.H., Nomie, K.J., and Wharton, R.P. (2018). No significant regulation of bicoid mRNA by Pumilio or Nanos in the early Drosophila embryo. PLoS One 13, e0194865. 10.1371/journal.pone.0194865.
(5) Wang, J., Zhang, S., Lu, H., and Xu, H. (2022). Differential regulation of alternative promoters emerges from unified kinetics of enhancer-promoter interaction. Nat Commun 13, 2714. 10.1038/s41467-022-30315-6.
(6) Xu, H., Sepulveda, L.A., Figard, L., Sokac, A.M., and Golding, I. (2015). Combining protein and mRNA quantification to decipher transcriptional regulation. Nat Methods 12, 739-742. 10.1038/nmeth.3446.
(7) Zhang, H., Wang, Y., Wu, X., Tang, X., Wu, C., and Lu, J. (2021). Determinants of genomewide distribution and evolution of uORFs in eukaryotes. Nat Commun 12, 1076. 10.1038/s41467-021-21394-y.
(8) Zhang, H., Dou, S., He, F., Luo, J., Wei, L., and Lu, J. (2018). Genome-wide maps of ribosomal occupancy provide insights into adaptive evolution and regulatory roles of uORFs during Drosophila development. PLoS Biol 16, e2003903. 10.1371/journal.pbio.2003903.
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Reviewer #1 (Public review):
Summary:
Wang et al. identify Hamlet, a PR-containing transcription factor, as a master regulator of reproductive development in Drosophila. Specifically, the fusion between the gonad and genital disc that is necessary for development of a continuous testes and seminal vesicle tissue essential for fertility. To do so, the authors generate novel Hamlet null mutants by CRISPR/Cas9 gene editing and characterize the morphological, physiological, and gene expression changes of the mutants using immunofluorescence, RNA-seq, cut-tag, and in-situ analysis. Thus, Hamlet is discovered to regulate a unique expression program, which includes Wnt2 and Tl, that is necessary for testis development and fertility.
Strengths:
This is a rigorous and comprehensive study that identifies the Hamlet dependent gene expression program mediating reproductive development in Drosophila. The Hamlet transcription targets are further characterized by Gal4/UAS-RNAi confirming their role in reproductive development. Finally, the study points to a role for Wnt2 and Tl as well as other Hamlet transcriptionally regulated genes in epithelial tissue fusion.
Weaknesses:
None noted.
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Reviewer #2 (Public review):
Strengths:
Wang and colleagues successfully uncovered an important function of the Drosophila PRDM16/PRDM3 homolog Hamlet (Ham) - a PR domain containing transcription factor with known roles in the nervous system in Drosophila. To do so, they generated and analyzed new mutants lacking the PR domain, and also employed diverse preexisting tools. In doing so, they made a fascinating discovery: They found that PR-domain containing isoforms of ham are crucial in the intriguing development of the fly genital tract. Wang and colleagues found three distinct roles of Ham: (1) Specifying the position of the testis terminal epithelium within the testis, (2) allowing normal shaping and growth of the anlagen of the seminal vesicles and paragonia and (3) enabling the crucial epithelial fusion between the seminal vesicle and the testis terminal epithelium. The mutant blocks fusion even if the parts are positioned correctly. The last finding is especially important, as there are few models allowing one to dissect the molecular underpinnings of heterotypic epithelial fusion in development. Their data suggest that they found a master regulator of this collective cell behavior. Further, they identified some of the cell biological players downstream of Ham, like for example E-Cadherin and Crumbs. In a holistic approach, they performed RNAseq and intersected them with the CUT&TAG-method, to find a comprehensive list of downstream factors directly regulated by Ham. Their function in the fusion process was validated by a tissue-specific RNAi screen. Meticulously, Wang and colleagues performed multiplexed in situ hybridization and analyzed different mutants, to gain a first understanding of the most important downstream-pathways they characterized - which are Wnt2 and Toll.
This study pioneers a completely new system. It is a model for exploring a process crucial in morphogenesis across animal species, yet not well-understood. Wang and colleagues not only identified a crucial regulator of heterotypic epithelial fusion but took on the considerable effort of meticulously pinning down functionally important downstream effectors by using many state-of-the-art methods. This is especially impressive, as dissection of pupal genital discs before epithelial fusion is a time-consuming and difficult task. This promising work will be the foundation future studies build on, to further elucidate how this epithelial fusion works, for example on a cell biological and biomechanical level.
Weaknesses:
The developing testis-genital disc system has many moving parts. Myotube migration was previously shown to be crucial for testis shape. This means, that there is the potential of non-tissue autonomous defects upon knockdown of genes in the genital disc or the terminal epithelium, affecting myotube behavior which in turn affects epithelial fusion, as myotubes might create the first "bridge" bringing the two epithelia together. Nevertheless, this is outside the scope of this work and could be addressed in the future.
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Author response:
The following is the authors’ response to the original reviews
Reviewer #1 (Public review):
Summary:
Wang et al. identify Hamlet, a PR-containing transcription factor, as a master regulator of reproductive development in Drosophila. Specifically, the fusion between the gonad and genital disc is necessary for the development of continuous testes and seminal vesicle tissue essential for fertility. To do this, the authors generate novel Hamlet null mutants by CRISPR/Cas9 gene editing and characterize the morphological, physiological, and gene expression changes of the mutants using immunofluorescence, RNA-seq, cut-tag, and in-situ analysis. Thus, Hamlet is discovered to regulate a unique expression program, which includes Wnt2 and Tl, that is necessary for testis development and fertility.
Strengths:
This is a rigorous and comprehensive study that identifies the Hamlet-dependent gene expression program mediating reproductive development in Drosophila. The Hamlet transcription targets are further characterized by Gal4/UAS-RNAi confirming their role in reproductive development. Finally, the study points to a role for Wnt2 and Tl as well as other Hamlet transcriptionally regulated genes in epithelial tissue fusion.
We appreciate that the reviewer thinks our study is rigorous.
Weaknesses:
The image resolution and presentation of figures is a major issue in this study. As a nonexpert, it is nearly impossible to see the morphological changes as described in the results. Quantification of all cell biological phenotypes is also lacking therefore reducing the impact of this study to those familiar with tissue fusion events in Drosophila development.
In the revised version, we have improved the image presentation and resolution. For all the images with more than two channels, we included single-channel images, changed the green color to lime and the red to magenta, highlighted the testis (TE) and seminal vescicles to make morphological changes more visible.
We had quantification for marker gene expression in the original version, and now also included quantification for cell biological phenotypes which are generally with 100% penetrance.
Reviewer #2 (Public review):
Strengths:
Wang and colleagues successfully uncovered an important function of the Drosophila PRDM16/PRDM3 homolog Hamlet (Ham) - a PR domain-containing transcription factor with known roles in the nervous system in Drosophila. To do so, they generated and analyzed new mutants lacking the PR domain, and also employed diverse preexisting tools. In doing so, they made a fascinating discovery: They found that PR-domain containing isoforms of ham are crucial in the intriguing development of the fly genital tract. Wang and colleagues found three distinct roles of Ham: (1) specifying the position of the testis terminal epithelium within the testis, (2) allowing normal shaping and growth of the anlagen of the seminal vesicles and paragonia and (3) enabling the crucial epithelial fusion between the seminal vesicle and the testis terminal epithelium. The mutant blocks fusion even if the parts are positioned correctly. The last finding is especially important, as there are few models allowing one to dissect the molecular underpinnings of heterotypic epithelial fusion in development. Their data suggest that they found a master regulator of this collective cell behavior. Further, they identified some of the cell biological players downstream of Ham, like for example E-Cadherin and Crumbs. In a holistic approach, they performed RNAseq and intersected them with the CUT&TAG-method, to find a comprehensive list of downstream factors directly regulated by Ham. Their function in the fusion process was validated by a tissue-specific RNAi screen. Meticulously, Wang and colleagues performed multiplexed in situ hybridization and analyzed different mutants, to gain a first understanding of the most important downstream pathways they characterized, which are Wnt2 and Toll.
This study pioneers a completely new system. It is a model for exploring a process crucial in morphogenesis across animal species, yet not well understood. Wang and colleagues not only identified a crucial regulator of heterotypic epithelial fusion but took on the considerable effort of meticulously pinning down functionally important downstream effectors by using many state-of-the-art methods. This is especially impressive, as the dissection of pupal genital discs before epithelial fusion is a time-consuming and difficult task. This promising work will be the foundation future studies build on, to further elucidate how this epithelial fusion works, for example on a cell biological and biomechanical level.
We appreciate that the reviewer thinks our study is orginal and important.
Weaknesses:
The developing testis-genital disc system has many moving parts. Myotube migration was previously shown to be crucial for testis shape. This means, that there is the potential of non-tissue autonomous defects upon knockdown of genes in the genital disc or the terminal epithelium, affecting myotube behavior which in turn affects fusion, as myotubes might create the first "bridge" bringing the epithelia together. The authors clearly showed that their driver tools do not cause expression in myoblasts/myotubes, but this does not exclude non-tissue autonomous defects in their RNAi screen. Nevertheless, this is outside the scope of this work.
We thank the reviewer’s consideration of non-tissue autonomous defects upon gene knockdown. The driver, hamRSGal4, drives reporter gene expression mainly in the RS epithelia, but we did observe weak expression of the reporter in the myoblasts before they differentiate into myotubes. Thus, we could not rule out a non-tissue autonomou effect in the RNAi screen. So we now included a statement in the result, “Given that the hamRSGal4 driver is highly expressed in the TE and SV epithelia, we expect highly effective knockdown occurs only in these epithelial cells. However, hamRSGal4 also drives weak expression in the myoblasts before they differentiated into myotubes (Supplementary Fig. 5B), which may result in a non-tissue autonomous effect when knocking down the candidate genes expressed in myoblasts.”
However, one point that could be addressed in this study: the RNAseq and CUT&TAG experiments would profit from adding principal component analyses, elucidating similarities and differences of the diverse biological and technical replicates.
Thanks for the suggestion. We now have included the PCA analyses in supplementary figure 6A-B and the corresponding description in the text. The PCA graphs validated the consistency between biological replicates of the RNA-seq samples. The Cut&Tag graphs confirm the consistency between the two biological replicates from the GFP samples, but show a higher variability between the w1118 replicates. Importantly, we only considered the overlapped peaks pulled by the GFP antibody from the ham_GFP genotype and the Ham antibody from the wildtype (w1118) sample as true Ham binding sites.
Recommendations for the authors:
Reviewer #1 (Recommendations for the authors):
Major Concern:
(1) The image resolution and presentation of figures (Figures 2, 5, 6, and 7) is a major issue in this study. As a non-expert, it is nearly impossible to see the morphological changes as described in the results. Images need to be captured at higher resolution and zoomed in with arrows denoting changes as described. Individual channels, particularly for intensity measurement need to be shown in black and white in addition to merged images. Images also need pseudo-colored for color-blind individuals (i.e. no red-green staining).
The images were captured at a high resolution, but somehow the resolution was drammaticlly reduced in the BioRxiv PDF. We try to overcome this by directly submitting the PDF in the Elife submission system. In the revised version, we have included single-channel images, changed the green and red colors to lime and magenta for color blindness. We also highlighted the testis (TE) and seminal vescicle structures in the images to make morphological changes more visible.
(2) The penetrance of morphological changes observed in RT development is also unclear and needs to be rigorously quantified for data in Figures 2, 5, and 7.
We now included quantification for cell biological phenotypes which are generally with 100% penetrance. The percentage of the penetrance and the number of animals used are indicated in each corresponding image.
Reviewer #2 (Recommendations for the authors):
Major Points
(1) Lines 193- 220 I would strongly suggest pointing out the obvious shape defects of the testes visible in Figure 2A ("Spheres" instead of "Spirals"). These are probably a direct consequence of a lack in the epithelial connection that myotubes require to migrate onto the testis (in a normal way) as depicted in the cartoons, allowing the testis to adopt a spiral shape through myotube-sculpting (Bischoff et al., 2021), further confirming the authors' findings!
Good point. In the revised text, we have added more description of the testis shape defects and pointed out a potential contribution from compromised myotube migration.
(2) Line 216: "Often separated from each other". Here it would be important to mention how often. If the authors cannot quantify that from existing data, I suggest carrying it out in adult/pharate adult genital tracts (if there is no strong survivor bias due to the lethality of stronger affected animals), as this is much easier than timing prepupae. This should be a quick and easy experiment.
Because it is hard to tell whether the separation of the SV and TE was caused by developmental defects or sometimes could be due to technical issues (bad dissection), we now change the description to, “control animals always showed connected TE and SV, whereas ham mutant TE and SV tissues were either separated from each other, or appeared contacted but with the epithelial tubes being discontinuous (Fig. 2B).” Additionally, we quantified the disconnection phenotype, which is 100% penetrance in 18 mutant animals. This quantification is now included in the figure.
(3) Lines 289-305, Figure 3. I could only find how many replicates were analyzed in the RNAseq/CUT&Tag experiments in the Material & Methods section. I would add that at least in the figure legends, and perhaps even in the main text. Most importantly, I would add a Principal Component Analysis (one for RNAseq and one for the CUT&TAG experiment), to demonstrate the similarity of biological replicates (3x RNaseq, 4x Cut&Tag) but also of the technical replicates (RNAseq: wt & wt/dg, ham/ham & ham/df, GD & TE; CUT&TAG: Antibody & GFP-Antibody, TG&TE...). This should be very easy with the existing data, and clearly demonstrate similarities & differences in the different types of replicates and conditions.
Principle component analysis and its description are now added to Supplementary Fig 6 and the main text respectively.
(4) Line 321; Supplementary Table 1: In the table, I cannot find which genes are down- or upregulated - something that I think is very important. I would add that, and remove the "color" column, which does not add any useful information.
In Supplementary table 1, the first sheet includes upregulated genes while the second sheet includes downregulated genes. We removed the column “color” as suggested.
(5) Line 409: SCRINSHOT was carried out with candidate genes from the screen. One gene I could not find in that list was the potential microtubule-actin crosslinker shot. If shot knockdown caused a phenotype, then I would clearly mention and show it. If not, I would mention why a shot is important, nonetheless.
shot is one of the candidate target genes selected from our RNA-seq and Cut&Tag data. However, in the RNAi screen, knocking down shot with the available RNAi lines did not cause any obvious phenotype. These could be due to inefficient RNAi knockdown or redundancy with other factors. We anyway wanted to examine shot expression pattern in the developing RS, give the important role of shot in epithelial fusion (Lee S., 2002). Using SCRINSHOT, we could detect epithelial-specific expression of shot, implying its potential function in this context. We now revised the text to clarify this point.
Minor points
(1) Cartoons in Figure 1: The cartoons look like they were inspired by the cartoon from Kozopas et al., 1998 Fig. 10 or Rothenbusch-Fender et al., 2016 Fig 1. I think the manuscript would greatly profit from better cartoons, that are closer to what the tissue really looks like (see Figure 1H, 2G), to allow people to understand the somewhat complicated architecture. The anlagen of the seminal vesicles/paragonia looks like a butterfly with a high columnar epithelium with a visible separation between paragonia/seminal vesicles (upper/lower "wing" of the "butterfly"). Descriptions like "unseparated" paragonia/seminal vesicle anlagen, would be much easier to understand if the cartoons would for example reflect this separation. It would even be better to add cartoons of the phenotypic classes too, and to put them right next to the micrographs. (Another nitpick with the cartoons: pigment cells are drastically larger and fewer in number (See: Bischoff et al., 2021 Figure 1E & MovieM1).)
Thanks for the suggestion. We have updated Figure 1 by adding additional illustrations showing the accessory gland and seminal vesicle structures in the pupal stage and changing the size of pigment cells.
(2) Line 95-121 I would also briefly introduce PR domains, here.
We have added a brief descripition of the PR domains.
(3) Line 152, 158, 160, 162. When first reading it, I was a bit confused by the usage of the word sensory organ. I would at least introduce that bristles are also known as external mechanosensory organs.
We have now revised the description to “mechano-sensory organ”.
eg. Line 184, 194, and many more. Most times, the authors call testis muscle precursors "myoblasts". This is correct sometimes, but only when referring to the stage before myoblast-fusion, which takes place directly before epithelial fusion (28 h APF). Postmyoblast-fusion (eg. during migration onto the testis), these cells should be called myotubes or nascent myotubes, as the fly muscle community defined the term myoblast as the singlenuclei precursors to myotubes.
We have now revised the description accordingly.
(4) Line 217/Figure 2B. It looks like there is a myotube bridge between the testis and the genital disc. I would point that out if it's true. If the authors have a larger z-stack of this connection, I suggest creating an MIP, and checking if there are little clusters of two/three/four nuclei packed together. This would clearly show that the cells in between are indeed myotubes (granted that loss of ham does not introduce myoblast-fusion-defects).
We do not have a Z-stack of this connection, and thus can not confirm whether the cells in this image are myotubes. However, we found that mytubes can migrate onto the testis and form the muscular sheet in the ham mutant despite reduced myotube density. At the junction there are myotubes, suggesting that loss of ham does not introduce myoblast-fusion defects. These results are now included in the revised manuscript, supplementary Fig. 5 C-D.
(5) Line 231/Supplementary Fig. 3C-G: I would add to the cartoons, where the different markers are expressed.
We have added marker gene expression in the cartoons.
(6) Line 239. I don't see what Figure 1A/1H refers to, here. I would perhaps just remove it.
Yes, we have removed it.
(7) Line 232. I would rephrase the beginning of the sentence to: Our data suggest Ham to be...
Yes, we have revised it.
(8) Line 248-250/Figure 2F. Clonal analyses are great, but I think single channels should be shown in black and white. Also, a version without the white dashed line should be shown, to clearly see the differences between wt and ham-mutant cells.
Now single channel images from the green and red images are presented in Supplementary Figures. This particular one is in Supplementary Figure 3B.
(9) Line 490. The Toll-9 phenotype was identified on the sterility effect/lack-of-spermphenotype alone, and it was deduced, that this suggests connection defects. By showing the right focus plane in Fig S8B (lower right), it should be easy to directly show whether there is a connection defect or not. Also, one would expect clearer testis-shaping defects, like in ham-mutants, as a loss of connection should also affect myotube migration to shape the testis. This is just a minor point, as it only affects supplementary data with no larger impact on the overall findings, even if Toll-9 is shown not to have a defect, after all.
We find that scoring defects at the junction site at the adult stage is difficult and may not be always accurate. Instead, we score the presence of sperms in the SV, which indirectly but firmly suggests successful connection between the TE and SV. We have now included a quantification graph, showing the penetrance of the phentoype in the new Supplementary Fig.14C. There were indeed morphological defects of TE in Toll-9 RNAi animals. We now included the image and quantification in the new Supplementary Fig.14B.
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Author response:
The following is the authors’ response to the original reviews
Public Reviews:
Reviewer #1 (Public Review):
This study investigates the role of microtubules in regulating insulin secretion from pancreatic islet beta cells. This is of great importance considering that controlled secretion of insulin is essential to prevent diabetes. Previously, it has been shown that KIF5B plays an essential role in insulin secretion by transporting insulin granules to the plasma membrane. High glucose activates KIF5B to increase insulin secretion resulting in the cellular uptake of glucose. In order to prevent hypoglycemia, insulin secretion needs to be tightly controlled. Notably, it is known that KIF5B plays a role in microtubule sliding. This is important, as the authors described previously that beta cells establish a peripheral sub-membrane microtubule array, which is critical for the withdrawal of excessive insulin granules from the secretion sites. At high glucose, the sub-membrane microtubule array is destabilized to allow for robust insulin secretion. Here the authors aim to answer the question of how the peripheral array is formed. Based on the previously published data the authors hypothesize that KIF5B organizes the sub-membrane microtubule array via microtubule sliding.
General comment:
This manuscript provides data that indicate that KIF5B, like in many other cells, mediates microtubule sliding in beta cells. This study is limited to in vitro assays and one cell line. Furthermore, the authors provide no link to insulin secretion and glucose uptake and the overall effects described are moderate. Finally, the overall effect of microtubule sliding upon glucose stimulation is surprisingly low considering the tight regulation of insulin secretion. Moreover, the authors state "the amount of MT polymer on every glucose stimulation changes only slightly, often undetectable…. In fact, we observe a prominent effect of peripheral MT loss only after a long-term kinesin depletion (three-four days)". This challenges the view that a KIF5Bdependent mechanism regulating microtubule sliding plays a major role in controlling insulin secretion.
(1) Our initial study was indeed done in a cell line, which is a normal approach to addressing molecular mechanisms of a phenomenon in a challenging cell model: primary pancreatic beta cells are prone to rapidly dedifferentiate outside of the organism and are hard to genetically modify. To address this reviewer’s comment, in the revised manuscript we now confirm the phenotype in beta cells within intact pancreatic islets from a KIF5B KO mouse model (New Figure 2 – Supplemental Figure 1).
(2) We agree that testing the effect of microtubule sliding on insulin secretion is an important question. Unfortunately, the experimental design needed to accomplish this task is not straighDorward. Importantly, besides microtubule sliding, KIF5B is heavily engaged in insulin granule transport, and GSIS deficiency upon KIF5B inactivation is well documented (e.g. Varadi et al 2002). In this study, we choose not to repeat this GSIS assay because of ample existing data. However, this reported GSIS deficiency could result from a combination of lack of insulin granule delivery to the periphery (previous data) and from the depletion of insulin granules from the periphery due to the loss of the submembrane MT bundle (this study and Bracey et al 2020). In order to exclusively test the role of MT sliding in secretion, a significant investment in mutant tool development would be needed. Ideally, a new mutant mouse model where insulin granule transport is allowed by MT sliding in blocked must be developed to specifically address this question. To conclude, answering this question will be the subject for another, follow-up study.
(3) We respecDully disagree with the reviewer’s opinion that the effect of MT sliding in beta cells is moderate. As MT networks go, even a slight change in MT configuration often has dramatic consequences. For example, in mitotic spindles, a tiny overgrowth of microtubule ends during metaphase, which causes them to attach to both kinetochores rather than just one, is very significant for the efficiency of chromosome segregation, causing aneuploidy and cancer. The changes in beta-cell MT networks that we are reporting are much stronger: the effect on the peripheral MT network accumulated over three days of KIF5B depletion is dramatic (Fig 2 B, C). Short-term gross MT network configurations after a single glucose stimulation are harder to detect, but MTs at the cell periphery are, in fact, destabilized and fragmented, as we and others have previously reported (Ho et al 2020, Mueller et al 2021). Preventing this MT rearrangement completely blocks GSIS (Zhu et al 2015, Ho et al 2020).
One of the most fascinating features of insulin secretion regulation is that the amount of generated insulin granules significantly exceeds the normal physiological needs for insulin secretion (~100 times more than needed). At the same time, even slightly facilitated glucose depletion can be devastating. Accordingly, the excessive insulin content of a beta cell resulted in the development of multiple levels of control, preventing excessive secretion. Our previous data suggest that the peripheral MT array provides one of those mechanisms. This study indicates that microtubule sliding is necessary to form the proper peripheral network in the long term. Short-term glucose-induced changes in the peripheral MT array likely need to be subtle to prevent over-secretion. Thus, we are not surprised that a dramatic effect of sliding inhibition is only detectable by our approaches after the changes in the MT network accumulate over time. In the revised paper, we now discuss the potential impact of peripheral MT sliding on positive and negative regulation of secretion and add a schematic model illustrating these processes.
Specific comments:
(1) Notably, the authors have previously reported that high glucose-induced remodeling of microtubule networks facilitates robust glucose-stimulated insulin secretion. This remodeling involves the disassembly of old microtubules and the nucleation of new microtubules. Using real-time imaging of photoconverted microtubules, they report that high levels of glucose induce rapid microtubule disassembly preferentially in the periphery of individual β-cells, and this process is mediated by the phosphorylation of microtubule-associated protein tau. Here, they state that the sub-membrane microtubule array is destabilized via microtubule sliding. What is the relevance of the different processes?
In this comment, the summary of our previous conclusions is correct, but the conclusion of this current study is re-stated incorrectly. Indeed, we have previously shown that in high glucose, MTs are destabilized at the cell periphery and nucleated in the cell interior. However, this current paper does not state that “the sub-membrane microtubule array is destabilized via microtubule sliding”. To answer this reviewer’s question, our data support a model where, during glucose stimulation, MT sliding within the peripheral bundle might move fragments of MTs severed by other mechanisms. Importantly, we propose that MT sliding restores the partially destabilized peripheral bundle by delivery of MTs that are nucleated at the cell interior and incorporating them into that bundle. In our overall model, three processes (destabilization, nucleation, and sliding to restore the bundle) are coordinated to maintain beta cell fitness on each GSIS cycle.
(2) On one hand the authors describe how KIF5B depletion prevents sliding and the transport of microtubules to the plasma membrane to form the sub-membrane microtubule array. This indicates KIF5B is required to form this structure. On the other hand, they describe that at high glucose concentration, KIF5B promotes microtubule sliding to destabilize the sub-membrane microtubule array to allow robust insulin secretion. This appears contradictory.
We never intended to make an impression that MT sliding destabilized the sub-membrane bundle. Apologies if there was a reason in our wording that caused this misunderstanding of our model. We propose that while the bundle is destabilized downstream of glucose signaling (e.g. due to tau phosphorylation, please see Ho et al Diabetes 2020), MT sliding remodels the bundle and thereafter rebuilds it to prevent over-secretion. In the revised manuscript, we have doublechecked the whole text to make sure that such misunderstanding is avoided.
(3) Previously, it has been shown that KIF5B induces tubulin incorporation along the microtubule shaft in a concentration-dependent manner. Moreover, running KIF5B increases microtubule rescue frequency and unlimited growth of microtubules. Notably, KIF5B regulates microtubule network mass and organization in cells (PMID: 34883065). Consequently, it appears possible that the here observed phenomena of changes in the microtubule network might be due to alterations in these processes.
We thank the reviewer for proposing this alternative explanation to the observed change in microtubule networks after KIF5B depletion. We have now directly tested this possibility. Namely, we have re-expressed the kinesin-1 motor domain in MIN6 cells depleted of KIF5B. This motor domain construct by itself is not capable of driving microtubule sliding because it lacks the tail domain. At the same time, it is known to move very efficiently at microtubules and should provide the effects as reported in the article cited by the reviewer. We found that the reexpression of the kinesin motor domain does not rescue microtubule network defects in beta cells (see new Figure 2 – Supplemental Figure 2). Thus, we conclude that the effects of kinesin depletion on the microtubule network in beta cells are due to the lack of microtubule sliding, as reported here.
(4) The authors provide data that indicate that microtubule sliding is enhanced upon glucose stimulation. They conclude that these data indicate that microtubule sliding is an integral part of glucose-triggered microtubule remodeling. Yet, the authors fail to provide any evidence that this process plays a role in insulin secretion or glucose uptake.
We would like to point out that we do not “fail” but rather choose not to overload our study by repeating insulin secretion assays in KIF5B-inactivated cells because this would not have been very informative. It has been found previously that kinesin-1 inactivation or knockout significantly attenuates insulin secretion because kinesin-1 is actively transporting insulin granules and kinesin-1 activity is enhanced under high glucose conditions (e.g. Varadi et al 2002, Cui et al., 2011, Donelan et al, 2002). That said, our current finding is very much in line with these previous data. When kinesin is depleted, two things would be happening at the same time: in the absence of sub-membrane microtubule bundle pre-existing insulin granules would be over-secreted, and new insulin would not be delivered to the periphery, both decreasing GSIS. Unfortunately, we do not have tools yet that would allow us to dissect which part of the insulin secretion defect is due to prior over-secretion (the consequence of deficient MT sliding) and which part is due to the lack of new granule delivery. We plan to develop such tools in the future and elaborate on them in a follow-up study. Here, our goal is to understand microtubule organization principles in beta cells, and we choose not to extend the scope of the current study to metabolic assays.
(5) The authors speculate that the sub-membrane microtubule array prevents the over-secretion of insulin. Would one not expect in this case a change in the distribution of insulin granules at the plasma membrane when this array is affected? Or after glucose stimulation? Notably, it has been reported that "the defects of β-cell function in KIF5B mutant mice were not coupled with observable changes in islet morphology, islet cell composition, or β-cell size" and "the subcellular localization of insulin vesicles was found to not be affected significantly by the decreased Kif5b level. The cytoplasm of both wild-type and mutant β-cells was filled with insulin vesicles. Insulin vesicle numbers per square μm were determined by counting all insulin vesicles in randomly photographed β-cells. More insulin granules were found in Kif5b knockout β-cells compared with control cells. This phenomenon is consistent with the observation that insulin secretion by β-cells is affected" whereby "Insulin vesicles (arrowheads) were distributed evenly in both mutant and control cells" (PMID: 20870970).
Quantitative analyses in the study cited by the reviewer do not include assays that would be relevant to our study. Particularly, in that study neither the amount of insulin granules at the cell periphery nor the ratio between the number of granules at the periphery and the beta cell interior has been analyzed. In addition, in our preliminary observations not shown here, insulin content in beta cells in KIF5B KO mice is highly heterogeneous, with a subpopulation of cells severely depleted of insulin. This opens a new avenue of investigation into beta cell heterogeneity, which is out of the scope of this current study. Thus, we chose to restrict this current study to microtubule organization data.
(6) Does the sub-membrane microtubule array exist in primary beta cells (in vitro and/or in vivo) and how it is affected in KIF5B knockout mice?
Yes, it does exist. In fact, we have first reported it in mouse islets (Bracey et al 2020, Ho et al 2020). Now, we report that the sub-membrane bundle is defective, and microtubules are misaligned in KIF5B KO mice (new Figure 2 – Supplemental Figure 1).
Reviewer #2 (Public Review):
In this article, Bracey et al. provide insights into the factors contributing to the distinct arrangement observed in sub-membrane microtubules (MTs) within mouse β-cells of the pancreas. Specifically, they propose that in clonal mouse pancreatic β-cells (MIN6), the motor protein KIF5B plays a role in sliding existing MTs towards the cell periphery and aligning them with each other along the plasma membrane. Furthermore, similar to other physiological features of β-cells, this process of MTs sliding is enhanced by a high glucose stimulus. Because a precise alignment of MTs beneath the cell membrane in β-cells is crucial for the regulated secretion of pancreatic enzymes and hormones, KIF5B assumes a significant role in pancreatic activity, both in healthy conditions and during diseases.
The authors provide evidence in support of their model by demonstrating that the levels of KIF5B mRNA in MIN6 cells are higher compared to other known KIFs. They further show that when KIF5B is genetically silenced using two different shRNAs, the MT sliding becomes less efficient. Additionally, silencing of KIF5A in the same cells leads to a general reorganization of MTs throughout the cell. Specifically, while control cells exhibit a convoluted and non-radial arrangement of MTs near the cell membrane, KIF5B-depleted cells display a sparse and less dense sub-membrane array of MTs. Based on these findings, the Authors conclude that the loss of KIF5B strongly affects the localization of MTs to the periphery of the cell. Using a dominant-negative approach, the authors also demonstrate that KIF5B facilitates the sliding of MTs by binding to cargo MTs through the kinesin-1 tail binding domain. Additionally, they present evidence suggesting that KIF5B-mediated MT sliding is dependent on glucose, similar to the activity levels of kinesin-1, which increase in the presence of glucose. Notably, when the glucose concentrations in the culturing media of MIN6 cells are reduced from 20 mM to 5 mM, a significant decrease in MT sliding is observed.
Strengths:
This study unveils a previously unexplained mechanism that regulates the specific rearrangement of MTs beneath the cell membrane in pancreatic β-cells. The findings of this research have implications and are of significant interest because the precise regulation of the MT array at the secretion zone plays a critical role in controlling pancreatic function in both healthy and diseased states. In general, the author's conclusions are substantiated by the provided data, and the study demonstrates the utilization of state-of-the-art methodologies including quantification techniques, and elegant dominant-negative experiments.
Weaknesses:
A few relatively minor issues are present and related to data interpretation and the conclusions drawn in the study. Namely, some inconsistencies between what appears to be the overall and sub-membrane MT array in scramble vs. KIF5B-depleted cells, the lack of details about the sub-cellular localization of KIF5B in these cells and the physiological significance of the effect of glucose levels in beta-cells of the pancreas.
We thank the reviewer for this insighDul review. In the revised version, we provided re-worded and extended interpretations and conclusions to prevent any issues or misunderstandings. We trust that while some noted apparent inconsistencies may reflect the intrinsic heterogeneity of the beta cell population, all data presented here indicate the same trend in phenotypes. In the revised version, we have provided additional cell views and, in places, alternative representative images and videos, to clear out any apparent inconsistencies. We also would like to point out that we in fact reported KIF5B localization: not surprisingly, KIF5B predominantly localized to insulin granules and the punctate staining fills the whole cytoplasm (Figure 2A, bottom panel). However, as pointed out in detail in our response to reviewer 1, we choose to leave out an extensive study of the physiological and metabolic consequences of the reported microtubule network dynamics to a follow-up study.
Reviewer #3 (Public Review):
Prior work from the Kaverina lab and others had determined that beta-cells build a microtubule network that differs from the canonical radial organization typical in most mammalian cell types and that this organization facilitates the regulated secretion of insulin-containing secretory granules (IGs). In this manuscript, the authors tested the hypothesis that kinesin-driven microtubule sliding is an underlying mechanism that establishes a sub-membranous microtubule array that regulates IG secretion. They employed knock-down and dominant-negative strategies to convincingly show microtubule sliding does, in fact, drive the assembly of the sub-membranous microtubule band. They also used live cell imaging assays to demonstrate that kinesin-mediated microtubule sliding in beta-cells is triggered by extracellular high glucose. Overall, this is an interesting and important study that relates microtubule dynamics to an important physiological process. The experiments were rigorous and well-controlled.
We truly appreciate this reviewer’ opinion.
Recommendations for the authors:
Reviewer #1 (Recommendations For The Authors):
Figures:
(1) Figure 1:
a) Why can one not see here, and in most following images, the peripheral sub-membrane microtubule array? One can also not see an accumulation of microtubules in the cell interior.
Microtubule pattern in beta cells is variable, and the sub-membrane array is seen in the whole population to a variable extent (see directionality histogram in Figure 2E for statistics). In fact, an array of peripheral MTs parallel to the cell border is present in the example shown in Figure 1 and in all following control images. To make it clearer, we now show the pre-bleach images in Figure 1 D-F at a lower magnification, so that the differences in MT density at the cell periphery and cell center are more clearly seen: MTs lack at the periphery in KF5B-depleted but not the control cells.
b) 5 min appears to be a long time and enough time to polymerize a significant number of new microtubules.
We interpret this comment as the reviewer’s concern that in FRAP assays, fluorescently-labeled MTs moving into the bleached area might be newly polymerizing MTs rather than preexisting MT relocated into that area. However, this is not the case because newly polymerized MTs contain predominantly quenched “dark” tubulin molecules and only a small percent of fluorescent tubulin. These dim MTs are not included in MT sliding assay analysis, where a threshold for bright MTs is introduced. Now, we added more details for the quantification of these data to Materials and Methods section.
c) The overall effects appear minor. It is unclear how Fig. 1-Suppl-Fig.1, where no significant difference is shown, is translated into Figure 1 J and K showing a significant difference.
With all due respect, we do not agree that the effect is minor. Please see our response to the Public Review where we discuss the major consequences of MT defects in detail.
To answer this specific comment, we show that there are significant differences in the number of rapidly moving MTs (5-sec displacement over 0.3 µm) and in the amount of stationary MTs (5sec displacement is below 0.15 µm). There is no significant difference in the amount of slightly displaced MTs (displacements between 0.15 and 0.3 µm; the central part of the histogram). This might indicate that these slight displacements do not depend on kinesin-1 motor but rather are caused by experimental noise, pushing by moving organelles, and/or myosin-dependent forces in the cell. In the revised manuscript, we have this quantification more clearly detailed in Methods and included in Figure legends.
d) The authors utilize single molecule tracking to further strengthen their conclusion that KIF5B promotes microtubule sliding. The observed effects are weaker than the data obtained from photobleaching experiments. The videos clearly show that there is still significant movement also in KIF5B-depleted cells. If K560RigorE236A binds irreversibly to a microtubule and this microtubule is growing (not only by the addition of tubulin dimers to the plus end; see PMID: 34883065) wouldn't that also result in movement of the tagged K560RigorE236A? As KIF5B is also required in the transport of insulin granules, it should also label "interior microtubules". And in Video 2 it appears that pretty much all "labeled" microtubules are moving.
K560RigorE236A forms fiducial marks along the whole MTs lattice, as previously shown in (Tanenbaum et al., 2014). When it is bound to MT lattice, K560RigorE236A moves with the whole MT if it is being relocated. The mechanism described in (PMID: 34883065) appears to be absent or minor in beta cells (see Figure 2- Supplemental Figure 2), thus, even if this mechanism would displace already polymerized MTs, this is not happening in this cell type.
The reviewer is correct, K560RigorE236A does mark all MTs throughout a beta cell. All MTs are moving slightly in a living cell because they are pushed around by moving organelles, actin contractility, etc. MTs may also be slid by other MT-dependent motors (dynein against the membrane and such). So, it is not surprising that the MT network is “breezing,” and kinesindependent sliding is only a part of MT movement. What we show here is that the KIF5Bdependent MT sliding is responsible for a relatively “long-distance” relocation of MTs manifested in long, directional displacement of fiducial marks. This does not exclude other movements. This makes extraction of kinesin-dependent MT movements somewhat challenging, of course, that is why we needed to do those extensive analyses.
e) Figure 1 G to K is misleading, at least in the context of the provided videos. There are several microtubules that move extensively in shRNA#2-treated cells and overall there appears more movement in this cell as in the control cell. Figure 1I is clearly not representative of the movement shown in Video 2.
We apologize if our selection of representative movies/figures for this experiment was imperfect. Indeed, in all depleted cells, SunTag puncta still move to a certain extent, either due to incomplete depletion or to alternative intracellular forces dislocating microtubules. However, there is a clear difference in the fraction of persistently moving puncta (please see Figure 1K and histogram in Figure 1 - Supplemental Figure 1B). Unfortunately, when the number of SunTag puncta per a cell is variable, it sometimes prevents a good visual perception of the actual distribution of moving versus stationary microtubules. We now show an alternative representative movie for the Figure 1I and the corresponding Video 2, with a goal to compare cells with more consistent numbers of Sun-Tag puncta.
(2) Figure 2A.
a) This is the only image that clearly shows the existence of a sub-membrane microtubule array and the concentration of microtubules in the cell interior. The differences are unclear between the experimental setups including the length of cultivation and knockdown of KIF5B or expression of mutants.
We now provide a more detailed description of each image acquisition and processing in Materials and Methods. In brief, while the morphology of MT patterns is intrinsically variable in beta cells, all control cells have populated peripheral MTs that exhibit a more parallel configuration as compared to depletions and mutants.
b) The authors state "While control cells had convoluted non-radial MTs with a prominent sub-membrane array, typical for beta cells (Fig. 2A), KIF5B-depleted cells featured extra-dense MTs in the cell center and sparse reseeding MTs at the periphery (Fig. 2B, C)". Could that not be explained with the observation that "Kinesin-1 controls microtubule length" (PMID: 34883065)?
Thank you for this interesting alternative idea. It does not appear to be the case for beta cells.
Please see Figure 2-Supplemental Figure 2 and our response to Public Review Comment #3.
Also, our apologies for the typo in the original manuscript: this is “receding” nor “reseeding”.
(3) Figure 3:
a) This is an elegant way to determine whether KIF5B is involved in microtubule sliding independent of the fact that the effect appears very small.
Thank you!
b) The assay depends on ectopic expression of a dominant negative mutant. It appears important to show that KIFDNwt is high enough expressed to indeed block the binding of endogenous KIF5B. The authors need to provide a control for this. Furthermore, authors need to provide evidence that other functions of KIF5B are not impaired such as transport of insulin granules and tubulin incorporation or microtubule stability and length.
Expression of cargo-binding motor domains routinely causes a dominant-negative effect of their cargo transport. This exact construct has been used for the purpose of dominant-negative action previously (Ravindran et al., 2017). It does prevent the membrane cargo binding of KIF5B (Ravindran et al., 2017), thus the transport of insulin granules is also impaired in overexpression cells. Confirming this fact would not influence our study conclusions, so we chose not to repeat these assays for the sake of time.
c) N-numbers should be similar. The data for KIFDNmut are difficult to interpret with possibly 2 experiments showing little to no displacement and 3 showing displacement.
In the revised manuscript, additional data have been added to increase N-numbers.
(4) Figure 4 and supplements: The morphology of the KIFDNwt cells is greatly affected and this makes it difficult to say whether the effect on microtubules at the cell periphery is a direct or indirect effect.
Yes, these cells often have less spread appearance, obscuring visual perception of MT distribution. We have now replaced the image of KIFDNwt cell (Figure 4, Supplemental Figure 1 A) to a more visually representative example.
Things to do:
(1) Notably, the authors have previously reported that high glucose-induced remodeling of microtubule networks facilitates robust glucose-stimulated insulin secretion. This remodeling involves the disassembly of old microtubules and the nucleation of new microtubules. Here, they state that the sub-membrane microtubule array is destabilized via microtubule sliding. What is the relevance of the different processes? Please discuss these in the manuscript.
Thank you, we have now extended our discussion of these points and our prior findings. We have also added a schematic model figure for clarity (Figure 7).
(2) 5 min appears to be a long time and enough time to polymerize a significant number of new microtubules. Do the authors have any information about the speed of MT formation in MIN6 cells? Can the authors repeat this experiment by preventing MT polymerization? Or repeat the experiment with EB1/EB3 reporter to visualize microtubule growth in the same experimental setting?
While some MT polymerization will happen in this timeframe, newly polymerized MTs contain predominantly quenched “dark” tubulin molecules and only a small percent of fluorescent tubulin. These dim MTs are not included in MT sliding assay analysis, where a threshold for bright MTs is introduced. We apologize for initially omitting certain details from the FRAP assay analysis. Now these details have been added.
Are the microtubules shown on the cell surface (TIRF microscopy) or do we see here all microtubules?
Please see Materials and Methods for microscopy methods and image processing for each figure. Specifically, FRAP assays show a maximum intensity projection of spinning disk confocal stacks over 2.4µm in height (approximately the ventral half of a cell).
(3) Previously, it has been shown that KIF5B induces tubulin incorporation along the microtubule shaft in a concentration-dependent manner. Moreover, running KIF5B increases microtubule rescue frequency and unlimited growth of microtubules. Notably, KIF5B regulates microtubule network mass and organization in cells (PMID: 34883065). Consequently, it appears possible that the here observed phenomena of changes in the microtubule network might be due to alterations in these processes. Authors need to exclude these possibilities and discuss them.
Thank you for this interesting alternative idea. It does not appear to be the case for beta cells. Please see Figure 2-Supplemental Figure 2 and our response to Public Review Comment #3.
(4) It is important that the authors describe in the text and possibly in the figure legends the differences between the experimental set-ups including the length of cultivation and knock down of KIF5B or expression of mutants.
Thank you, please see these details in the text (Materials and Methods section).
(5) Figure 5: Does KIF5B depletion rescue the kinesore-induced defects
Thank you for suggesting this control. We have now conducted corresponding experiments. The answer is yes, it does. Kinesore does not induce detectable changes in MT patterns in KIF5Bdepleted cells (new Figure 5-Supplemental Figure 2).
(6) Can the authors block kinesin-1 resulting in microtubule accumulation in the cell center and then release the block, and best inhibiting microtubule formation, to see whether the microtubules accumulated in the cell center will be transported to the periphery?
This proposed experiment would have been a nice illustration to the study, however it has proven to be too challenging. Unfortunately we have to leave it for the future studies. However, the experiments already included in the paper are sufficient to prove our conclusions.
Minor comments:
(1) The English needs to be improved. Oaen it is unclear what the authors try to convey. The manuscript is difficult to read and contains several overstatements.
The revised manuscript has been through several rounds of proof-reading for clarity.
(2) It is important to describe in more detail in the introduction what is known about KIF5B in beta cells. Previously, it has been demonstrated that silencing, or inactivation by a dominant negative form of KIF5B, blocks the sustained phase of glucose-stimulated insulin secretion (PMID: 9112396, PMID: 12356920, PMID: 20870970).
Yes, this is of course very important and have been cited in the original manuscript. Now, we have expanded the discussion on the matter.
(3) Figure 1B and Fig. 1 Suppl Fig.1: Please provide band sizes and provide information on the size of KIF5B.
We have replaced Fig. 1B and Suppl Fig 1A with quantitative analysis of KIF5B depletion, not found in new Fig. 1B and Suppl Fig. 1A-C.
(4) It is important to state the used glucose concentrations in Figure 1D (based on the methods section it is probably 25 mM glucose) and all subsequent experiments. Is this correct and comparable to Figure 6A or B? For the non-specialized reader, more information should be provided on why initial glucose starvation is performed.
Cell culture models of pancreatic beta cells are routinely maintained at glucose levels that at considered “high”, or stimulatory for secretion. This is needed to prevent the loss of cells’ capacity to respond to glucose stimulation over generations. In order to test GSIS, cells need to be equilibrated at low (fasting, standardly 2.8mM) glucose levels for several hours, so that they are capable of secreting insulin upon glucose addition. 25mM glucose is normally used to stimulate GSIS in cell culture models of beta cells, like MIN6. This is a higher concentration as compared to what is needed to stimulate primary beta cells in islets.
Reviewer #2 (Recommendations For The Authors):
I have the following specific questions that pertain to data interpretation and the conclusions drawn.
(1) The morphology of the overall MT array before the bleach treatment in both control cells and KIF5B-KD cells depicted in Figure 1D-F and Figure 2A-C appears to be distinct. In Figure 1, it seems that the absence of KIF5B results in a general augmentation of MT mass, whereas the arrangement presented in Figure 2 indicates the contrary. Even in the sub-membrane areas, this phenomenon appears to hold true. However, the images used in this study, which depict entire cells or a significant portion of cells, may not be ideal for visualizing the sub-membrane regions.
It would be beneficial if the author could offer some explanations for this apparent inconsistency.
While beta cell population is intrinsically heterogeneous, all data presented here indicate the same trend in phenotypes. Possibly, some apparent inconsistency between figure 1 and 2 appeared because in the original manuscript we did not show the pre-bleach whole-cell overview in Figure 1. In the revised version, we now show the whole cells for pre-bleach so that MT organization at the cell periphery can be assessed. Please note that in the control cell, MTs are more or less equally distributed over the cell, while in KIF5B depletions the cell periphery is significantly less populated than the cell center. Furthermore, we did not detect MT mass augmentation or increase in KIF5B depletions. One possible explanation for such reviewer’s impression from Figure 2 is that Figure 2 F-H shows thresholded images where threshold was adjusted to highlight peripheral MTs in each cell. Please note that this is not the same threshold for each cell (see Figure 2 - Supplemental Figure 2 and 3). Thus, KIF5B-depleted cells that have fewer MTs at the periphery appear brighter in these thresholded images. For the true comparison of MT intensity, please see Figure 2 A-C (grayscale image, not the threshold).
(2) It would be helpful if the author could provide a visual representation or comment on the sub-cellular localization of KIF5B in MIN6 cells. Is it predominantly localized in the submembrane region, or is it more evenly distributed throughout the cytoplasm?
Please see Fig 2A, lower panel. KIF5B is seen across the cell as a punctate staining, in agreement with previous findings that it mostly localize at IGs.
(3) The alteration in microtubule (MT) organization and sliding in the absence of KIF5B seems to initiate in proximity to the apparent microtubule organizing center (MTOC) depicted in Figure 2A, and then "simply" extends towards the sub-membrane region. Although the authors acknowledge it, it would be advantageous for the readers to have a clearer indication that the sub-membrane microtubule (MT) reorganization in the absence of KIF5B is a result of a broader MT reorganization rather than a specific occurrence restricted to the sub-membrane regions.
Thank you for this comment. We now extend our discussion to clearer state our conclusions and interpretations of this point. We also have added a schematic Figure 7 as an illustration.
(4) Regarding the "glucose experiments," it is common to add 20-25 mM glucose to culture media, but physiological concentrations of glucose typically hover around 5 mM. Therefore, it is somewhat unclear what the implications are when investigating the impact of KIF5B depletion on MT sliding at 2.8 mM of glucose. It would be helpful if the authors could provide some commentary on this matter, particularly in relation to physiological and pathological conditions.
2.8 mM glucose is a standard low glucose condition used to model glucose deprivation/fasting. For functional primary beta cells within pancreatic islets, GSIS can be triggered by glucose stimulation as low as 8-12 mM glucose. However, for glucose stimulation of cultured beta cells such as MIN6 used in this paper, 20-25 mM glucose is standardly used because these cell lines have a higher threshold of stimulation compared to primary beta cells and whole islets.
(5) In supplementary Figure 1A, it would be helpful if the lanes in the WB were marked indicating what is what. In my observation, it appears that Supplementary Figure 1A, particularly lanes #2, 3, and 4, display the GAPDH protein (MW 36 kDa) (or is it alpha-tubulin, as mentioned in the Material and Methods section and indicated in lane #409?) relative to Figure 1A. I am curious about KIF5B (MW 108 kDa). Is it represented by the upper band? Did the author probe the same membrane simultaneously with two different primary antibodies? This should be clarified, and the author should indicate the molecular weight of the ladder.
Indeed, in the original WB two antibodies have been used together, due to a challenge in collecting a sufficient number of shRNA-expressing beta cells. It caused a confusion and improper interpretation of the loading control. We thank the reviewer for catching this. We have now replaced old Fig. 1B and Suppl. Fig. 1A with quantitative analysis of KIF5B depletion based on single-cell immunofluorescent staining. It is now found in new Fig. 1B and Suppl Fig. 1A-C.
Reviewer #3 (Recommendations For The Authors):
In all of the figures that present microtubule orientations (e.g. Figure 2E) the error bars obscure the vertical bins making them difficult to read or interpret. If they were rendered at a larger scale, it would be easier to read and interpret these results.
Thank you pointing this out. We now show these histograms with a different format of error bars and without outliers that obscure the view. A variant with outliers is now shown in the supplement.
Some of the callouts to the videos in the paper are inaccurate. Perhaps the authors reordered sections of the paper but failed to correctly renumber the video citations?
Thank you for this comment, we have corrected all callouts now.
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity (Required)):*
Summary: Chitin is a critical component of the extracellular matrix of arthropods and plays an essential role in the development and protection of insects. There are two chitin synthases in insects: Type A (exoskeletons) and Type B (for the peritrophic matrix in the gut). The study aims to investigate the specificity and mechanisms of the two chitin synthases in D. melanogaster and to clarify whether they are functionally interchangeable. Various genetic manipulations and fluorescence-based labeling were used to analyze the expression, localization, and function of Kkv and Chs2 in different tissues. Chs2 is expressed in the PR cells of the proventriculus and is required for chitin deposition in the peritrophic matrix. Kkv can deposit chitin in ectodermal tissues but not in the peritrophic matrix, whereas Chs2 can deposit chitin in the peritrophic matrix but not in ectodermal tissues. The subcellular localization of chitin synthases is specific to the tissues in which they are expressed. Kkv localizes apically in ectodermal tissues, whereas Chs2 localizes apically in the PR cells of the proventriculus. Altogether, Kkv and Chs2 cannot replace each other. The specificity of chitin synthases in D. melanogaster relies on distinct cellular and molecular mechanisms, including intracellular transport pathways and the specific molecular machinery for chitin deposition.*
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Congratulations on this incredible story and manuscript, which is straightforward and well-written. However, I have some comments that may help to improve it.
We thank the reviewer for this very positive comment. We have addressed all comments to clarify and improve our manuscript.
Major comments: 1.) Funny thing: the Chs2 mutant larva shows a magenta staining below the chitin accumulation of the esophagus, which looks like a question mark in 1H but cannot be found in control. Is that trachea reaching the pv?
We assume that the reviewer refers to Fig 1N. As the reviewer suspects, this corresponds to a piece of trachea. Figure 1N shows a single section, making it difficult to identify what this staining corresponds to. We are providing below a projection of several sections where it is easier to identify the staining as tracheal tissue (arrow).
We are now marking this pattern as trachea (tr) in the manuscript Figure 1N
2.) Also, though it is evident that the PM chitin is lost in Ch2 mutants, could it be that the region is disturbed and cells express somewhere else chitin? There are papers by Fuß and Hoch (e.g., Mech of Dev, 79, 1998; Josten, Fuß et al., Dev. Biol.267, 2004) using markers such as Dve, Fkh, Wg, Delta, and Notch, etc. for precisely marking the endodermal/ectodermal region in the embryonic foregut/proventriculus. It would be beneficial to show, along with chitin and Chs expression patterns, the ectoderm/endoderm cells. This is particularly important as the authors report endodermal expression of Chs2 in embryos but don't use co-markers of the endodermal cells.
We agree with the reviewer that this is an important issue and we note that Reviewer 2 also raised the same point. Therefore, we have addressed this issue.
We obtained an antibody against Dve, kindly provided by Dr. Hideki Nakagoshi. Dve marks the endodermal region in the proventriculus (Fuss and Hoch, 1998, Fuss et al., 2004, Nakagoshi et al., 1998).This antibody worked nicely in our dissected L3 digestive tracts and allowed us to mark the endodermal region. We also obtained an antibody against Fkh, kindly provided by Dr. Pilar Carrera. Fkh marks the ectodermal foregut cells (Fuss and Hoch, 1998, Fuss et al., 2004). While, in our hands, this antibody performed well in embryonic tissues, we observed no staining in our dissected L3 digestive tracts. The reason for this is unclear, but we suspect technical limitations may be responsible (the ectodermal region of the proventriculus is very internal, potentially hindering antibody penetration). To circumvent this inconvenience, we tested a FkhGFP tagged allele available in Bloomington Stock Center. Fortunately, we were able to detect GFP in ectodermal cells of L3 carrying this allele. Using this approach, we conducted experiments to detect Fkh and Dve in the wild type or in Df(Chs2) conditions (Fig S1). In addition, we used these markers to map the expression of Kkv and Chs2 in the proventriculus (Fig 4).
Altogether the results using these endodermal/ectodermal markers confirmed the presence of a cuticle adjacent to the FkhGFP-positive cells and a PM adjacent to the PR cells, marked by Dve. This PM is absent in Df(Chs2) L3 escapers, however, the general pattern of Fkh/Dve expression is not affected. Finally, we show that Chs2-expressing cells are positive for Dve while Kkv-expressing cells are not. We were unable to conduct an experiment demonstrating Kkv and Fkh co-expression due to technical incompatibilities, as both genes require the use of GFP-tagged alleles to visualise their expression. However, we believe that our imaging of Dve/Kkv clearly shows that Kkv expressing cells lack Dve expression and are localised in the internal (ectodermal) region of the proventriculus (Fig 4E).
3.) The origin of midgut chitin accumulation is unclear. Chitin can come from yeast paster. Can the authors check kkv and chs2 mutants for food passage and test starving L1 larvae to detect chitin accumulation in the midgut without feeding them?
This is a very interesting point that has also intrigued us.
We observed that, in addition to the PM layer lining the midgut epithelium, CBP staining also revealed a distinct luminal pattern. Our initial hypothesis was that this pattern corresponded to the PM. However, its presence in Df(Chs2) larval escapers clearly indicates that this is not the case. Unfortunately, we cannot assess this pattern in kkv mutants, as these die at eclosion and do not proceed to larva stages.
As the reviewer suggests, a likely possibility is that the luminal pattern originates from components in the food. These could correspond to yeast, as suggested by the reviewer, or possibly remnants of dead larvae present in the media (although Drosophila is considered herbivore in absence of nutritional stress).
To assess whether the luminal pattern originates from the food we conducted two independent experiments. In experiment 1, we collected larvae reared under normal food conditions. Newly emerged L3 larvae were transferred in small numbers to minimise cannibalism (Ahmad et al., 2015) to new Petri plates containing moist paper. Larvae were starved for 3,4 or 5 days. Larvae starved for more than 5 days did not survive. We then dissected the guts and analysed CBP staining. We observed the presence of luminal CBP staining in these larvae, along with the typical PM signal in the proventriculus and along the midgut. In experiment 2, we collected larvae directly on agar plates containing only agar (without yeast or any other nutrients). We allowed the larvae to develop. These larvae showed minimal growth. We dissected the guts of these small larvae (which were challenging to dissect) and analysed CBP staining. Again, we detected presence of luminal CBP staining.
These experiments indicate that, despite starvation, a luminal chitin pattern is still detected, suggesting that it is unlikely to originate from food. However, we cannot unequivocally rule out the possibility that the cannibalistic, detrivorous or carnivorous behavior of the nutrionally stressed larvae (Ahmad et al., 2015) in our experiments may influence the results. Therefore, more experiments would be required to address this point.
In summary, while we cannot provide a definitive answer to the reviewer's question, nor fully satisfy our own curiosity, we would like to note that this specific observation is unrelated to the main focus of our study, as we have confirmed that the luminal pattern is not dependent on Chs2 function.
Portions of midgut of starved larvae under the regimes indicated, stained for chitin (CBP, magenta). Note the presence of the luminal chitin pattern in the midgut
4.) Subcellular localization assays require improved analysis, such as a co-marker for the apical membrane and statistical analysis with co-localization tools, showing the overlap at the membrane and intracellularly with membrane co-markers and KDEL.
We have addressed the point raised by the reviewer. To analyse and quantify Chs2 subcellular localisation, particularly considering the observed pattern, we decided to use both a membrane and an ER marker. As a membrane marker we used srcGFP expressed in tracheal cells (see answer to point 7 of Reviewer 1) and as an ER marker we used KDEL. In this analysis, tracheal cells also expressed Chs2, which was visualised using the Chs2 antibody generated in the lab.
To assess the colocalisation of Chs2 with each marker we used the JaCop pluggin in Fiji. We analysed individual cells from different embryos stained for membrane/ER/Chs2 using single confocal sections (to avoid artificial colocalisation). Images were processed as described in Materials and Methods. We obtained the Pearson's correlation coefficient (r), which measures the degree of colocalisation, for Chs2/srcGFP and Chs2/KDEL, n=36 cells from 9 different embryos. The average r value for Chs2/srcGFP was 0,064, while the average for Chs2/KDEL was around 0,7. r ranges between -1 and 1, where 1 indicates perfect correlation, 0 no correlation, and -1 perfect anti-correlation. Typically, an r value of 0.7 and above is considered a strong positive correlation, whereas a value below 0,1 is regarded as very weak or no correlation. Thus, our colocalisation analysis supports the hypothesis that Chs2 is primarily retained in the ER when expressed in non-endogenous tissues, likely unable to reach the membrane.
We have reorganised the figures and now present an example of Chs2/srcGFP/KDEL subcellular localisation in tracheal cells and the colocalisation analysis in Fig 5H. The colocalisation analysis is described in the Materials and Methods section.
Minor comments:
5.) The authors used "L3 larval escapers." It would be interesting to know if the lack of Chs2 and the peritrophic matrix cause any physiological defects or lethality.
The point raised by the reviewer is very interesting and relevant. The peritrophic matrix is proposed to play several important physiological roles, including the spatial organisation of the digestive process, increasing digestive efficiency, protection against toxins and pathogens, and serving as a mechanical barrier. Therefore, it is expected that the absence of chitin in the PM of the Df(Chs2) larval escapers may cause various physiological effects.
Analysing these effects is a complex task, and it constitutes an entire research project on its own. In addressing the physiological requirements of the PM, we aim to analyse adult flies and assess various parameters, including viability, digestive transit dynamics, gut integrity, resistance to infections, fitness and fertility.
A critical initial challenge in conducting a comprehensive analysis of the physiological requirements of the PM is identifying a suitable condition to evaluate the absence of Chs2. In this work we are using a combination of two overlapping deficiencies that uncover Chs2, along with a few additional genes (as indicated in Fig S1F). This deficiency condition presents two major inconveniences: first, the observed defects could be caused or influenced by the absence of genes other than Chs2, preventing us from conclusively attributing the defects to Chs2 loss (unless we rescued the defects by adding Chs2 back as we did in the manuscript). Second, the larva escapers, which are rare, do not survive to adulthood (indicating lethality but preventing us from analysing specific physiological aspects).
To overcome these limitations, we are currently working to identify a genetic condition in which we can specifically analyse the absence of Chs2. We have identified several available RNAi lines and we are testing their efficiency in preventing chitin deposition in the PM. Additionally, we are characterising a putative null Chs2 allele, Chs2CR60212-TG4.0. This stock contains a Trojan-GAL4 gene trap sequence in the third intron, inserted via CRISPR/Cas9. As described in Flybase (https://flybase.org/), the inserted cassette contains a 'Trojan GAL4' gene trap element composed of a splice acceptor site followed by the T2A peptide, the GAL4 coding sequence and an SV40 polyadenylation signal. When inserted in a coding intron in the correct orientation, the cassette should result in truncation of the trapped gene product and expression of GAL4 under the control of the regulatory sequences of the trapped gene. We already know that, when crossed to a reporter line (e.g. UAS-GFP or UAS-nlsCherry) this line reproduces the Chs2 expression pattern, suggesting that the insertion may generate a truncated Chs2 protein. This line would represent an ideal tool to assess the absence of Chs2, and we are currently characterising it for further analysis
In summary, we fully agree with the reviewer that investigating the physiological requirements of the PM is a compelling area of research, and we are actively addressing this question. However, this investigation constitutes a substantial and independent research effort that we believe is beyond the scope of the current manuscript at this stage.
6.) The order identifiers are missing for materials and antibodies, e.g., anti-GFP (Abcam), but Abcam provides several ant-GFP; which was used? Please provide order numbers that guarantee the repeatability for others.
We have now added all identifiers for materials and reagents used, in the materials and methods section.
7.) Figure S5C, C', what marks GFP (blue) in the trachea? Maybe I have overlooked the description. What is UASsrcGFP? What is the origin of this line?
We apologise for not providing a more detailed description of the UASsrcGFP line. This line corresponds to RRID BDSC#5432, as now indicated in Materials and Methods section.
In this transgene, the UAS regulatory sequences drive the expression of GFP fused to Tag:Myr(v-src). As described in Flybase (https://flybase.org/), the P(UAS-srcEGFP) construct contains the 14 aa myristylation domain of v-src fused to EGFP. This tag is commonly used to target proteins of interest to the plasma membrane. The construct was generated by Eric Spana and is available in Drosophila stock centers.
We typically use this transgene as a plasma membrane marker to outline cell membrane contours. In our experiments, srcGFP, under the control of the btlGal4 promoter, was used to visualise the membrane of tracheal cells in relation to Chs2 accumulation. As indicated in point 4, we have now transferred the images of srcGFP/Chs2/KDEL to the main Figures and used it for colocalisation analyses.
8.) The authors claim that they validated the anti-Chs2 antibody. However, they show only that it recognizes a Cht2 epitope via ectopic expression. For more profound validation, immune staining is required in deletion mutants, upon knockdown, or upon expression of recombinant proteins, which is not shown.
We generated an antibody against Chs2. We found that the antibody does not reliably detect the endogenous Chs2 protein, and so we find no pattern in the proventriculus or any other tissue in our immunostainings. It is very possible that the combination of low endogenous levels of Chs2 with a sub-optimal antibody (or low titer) leads to this result. In any case, as the antibody does not detect endogenous Chs2, it cannot be validated by analysing the expression upon Chs2 knockdown. In contrast, our antibody clearly detects specific staining in various tissues (e.g. trachea, salivary glands, gut) when Chs2 is expressed using the Gal4/UAS system, confirming its specificity for Chs2. It is worth to point that it is not unusual to find antibodies that are not sensitive enough to detect endogenous proteins but can detect overexpressed proteins (e.g
(Lebreton and Casanova, 2016)).
As an additional way to validate the specificity of our antibody, we have used the chimeras generated, as suggested by the reviewer. As indicated in the Materials and Methods section, the Anti-Chs2 was generated against a region comprising 1222-1383 aa in Chs2, with low homology to Kkv. This region is present in the kkv-Chs2GFP chimera but absent in Chs2-KkvGFP (see Fig 7A). Accordingly, our antibody recognises kkv-Chs2GFP but does not recognise Chs2-KkvGFP (Fig S7).
We have revised the text in chapter 6 (6. Subcellular localisation of Chs2 in endogenous and ectopic tissues) to clarify these points and we have added the validation of the antibody using the chimeras in chapter 8 (8. Analysis of Chs2-Kkv chimeras) and Fig S7
9) The legend and text explaining Fig. 4 D-E' can be improved. The authors used the Crimic line, which is integrated into the third ("coding") intron. This orientation can lead to the expression of Gal4 and cause a truncated version of the protein (according to Flybase). Is Chs2 expression reduced in the crimic mutant? If the mutation causes expression of a truncated version, the Chs2 antibody may not be able to detect it as it recognizes a fragment between 1222 and 1383 aa? Also, I'm unsure whether the Chs2 antibody or GFP was used to detect expression in PR cells. The authors describe using Ch2CR60212>SrcGFP together with Chs2+ specific antibodies.
We apologise for the confusion.
As the reviewer points, Chs2CR60212-TG4.0 contains a Trojan-GAL4 gene trap sequence in the third intron, inserted via CRISPR/Cas9. As described in Flybase (https://flybase.org/), the inserted cassette contains a 'Trojan GAL4' gene trap element composed of a splice acceptor site followed by the T2A peptide, the GAL4 coding sequence and an SV40 polyadenylation signal. When inserted in a coding intron in the correct orientation, the cassette should result in truncation of the trapped gene product and expression of GAL4 under the control of the regulatory sequences of the trapped gene.
We found that when crossed to UAS-GFP or UAS-nlsCherry, this line reproduces a expression pattern that must correspond to Chs2. As the antibody that we generated is not suitable for detecting Chs2 endogenous expression, we resorted to using this combination, Chs2CR60212-TG4.0 crossed to a reporter line (such asUAS-GFP or UAS-nlsCherry), to visualise Chs2 expression by staining for GFP/Cherry in the intestinal tract and in the embryo (Figures 4 and S4).
We realise that the Figure labelling we used in our original submission is very misleading, and we apologise for this. In the original figures we had labelled the staining combination with Kkv, Chs2, Exp as if we had used these antibodies. However, in all cases, we used GFP to visualise the pattern of these proteins in the genetic combinations indicated in the figures. We have corrected this in our revised version. We have also updated the text (Chapter 5), figures and figure legends.
As the reviewer points, the insertion in Chs2CR60212-TG4.0 is likely to generate a truncated Chs2 protein. We cannot confirm this using the Chs2 antibody we generated because it does not recognise the endogenous Chs2 pattern. Nevertheless, as indicated in point 5, we are currently characterising this line. Our preliminary results indicate a high complexity of effects from this allele that require thorough analysis, as it may be acting as a dominant negative.
Reviewer #1 (Significance (Required)):
Significance: The manuscript's strength and most important aspects are the genetic analysis, expression, and localization studies of the two Chitin synthases in Drosophila embryos and larvae. However, beyond this manuscript, the development of mechanistic details, such as interaction partners that trigger secretion and action at the apical membranes and the role of the coiled-coil domain, will be interesting.
The manuscript uses "first-class" genetics to describe the different roles of the two Chitin synthases in Drosophila, comparing ectodermal chitin (tracheal and epidermal chitin) with endodermal (midgut) chitin. Such a precise analysis has not been investigated before in insects. Therefore, the study deeply extends knowledge about the role of Chitin synthases in insects.
The audience will specialize in basic research in zoology, developmental biology, and cell biology regarding - how the different Chitin synthases produce chitin. Nevertheless, as chitin is relevant to material research and medical and immunological aspects, the manuscript will be fascinating beyond the specific field and thus for a broader audience.
I'm working on chitin in the tracheal system and epidermis in Drosophila.
__Reviewer #2 (Evidence, reproducibility and clarity (Required)): __ Drosophila have two different chitin synthase enzymes, Kkv and Chs2, and due to unique expression patterns and mutant phenotypes, it is relatively clear that they have different functions in producing either the cuticle-related chitin network (Kkv) or the chitin associated with the peritrophic matrix (PM). However, what is unknown is whether the different functions in making cuticle vs PM chitin is related to differences in cellular expression and/or enzyme properties within the cell. The authors exploit the genetic tractability of Drosophila and their ability to image cuticle vs PM chitin production to examine whether these 2 enzymes can substitute each other. They conclude that these two proteins are not equivalent in their capacity to generate chitin. The data are convincing; however, it is currently presented in a subjective fashion, which makes it difficult to interpret. Additionally, in my opinion there is some interpretation that requires softening or alternatively interpreted.
We are pleased that the reviewer finds our data convincing. However, we acknowledge the reviewer's concern that our data was presented in a subjective manner, and we apologise for this. In response, we have carefully reviewed the entire manuscript and revised our data presentation to ensure a more objective tone. Numerous changes (including additional quantifications, new experiments and clarifications) have been incorporated throughout the text. These revisions are highlighted in the marked-up version. We hope that this revision provides a more accurate and objective presentation of our work.
Major Comments:
1- While the imaging is lovely, there are some things that are difficult to see in the figures. For example, the "continuous, thin and faint 'chitin' layer that lined the gut epithelium" is very difficult to visualise in the control images. Can they increase the contrast to help the reader appreciate this layer? This is particularly important as we are asked to appreciate a loss of this layer in the absence of Chs2.
We have tried to improve the figures so that the PM layer in the midgut region is more clearly visible. We have added magnifications of small sections at the midgut lumen/epithelium border in grey to help visualise the PM. These improvements have been made in Figures 1,2,S1,S2,S3 and we believe that they better illustrate our results.
2- All the mutant analysis is presented subjectively. For example, the authors state that they "found a consistent difference of CBP staining when they compared the 'Chs2' escapers to the controls". How consistent is consistent? Can this be quantified? What is the penetrance of this phenotype? They say that the thin layer is absent in the midgut and the guts are thinner. Could they provide more concrete data?
As indicated above, we have reviewed the text to provide a more objective description of the phenotypes.
We have quantified the defects in the Df(Chs2) mutant conditions. For this quantification we dissected intestinal tracts of control and Df(Chs2) larva escapers. We fixed, stained and mounted them together. The control guts expressed GFP in the midgut region as a way to distinguish control from mutants. We analysed the presence or absence of chitin in the PM. We found absence of chitin in the proventricular lumen and in the midgut in all Df(Chs2) guts and presence of chitin there in all control ones (n=12 Df(Chs2) guts, n=9 control guts, from 5 independent experiments). The results indicate a fully penetrant phenotype of lack of chitin in Df(Chs2) larva escapers (100% penetrance). We have added this quantification in the text, chapter 2 (2. Chs2 deposits chitin in the PM).
To quantify the thickness of the guts, we took measurements of the diameter in control and Df(Chs2) guts at two comparable distance positions from the proventriculus (position 1, position 2, see image). Our quantifications indicated thinner tubes in mutant conditions.
Image shows the anterior part of the intestinal tract, with the proventriculus encircled in white. Positions 1 and 2 indicate where the diameter quantifications were taken. Scatter plots quantifying the diameter at the two different positions in control and Chs2 larval escapers. Bars show mean {plus minus} SD. p=p value of unpaired t test two-tailed with Welch's correction.
However, we are aware that our analysis of the thickness of the gut is not accurate, because we have not used markers to precisely measure at the same position in all guts and because we have not normalised the measurement position in relation to the whole intestinal tract (mainly due to technical issues).
In relation to the fragility, we noticed that the guts of Chs2 larval escapers tended to break more easily during dissection than control guts, however, we have not been able to quantify this parameter in a reliable and objective manner.
Since we consider that the requirement of Chs2 for PM deposition is sufficiently demonstrated, and that aspects such as gut morphology or fragility relate to the physiological requirements of the PM, which we are beginning to address as a new independent project (see our response to point 5 of Reviewer 1), we have decided to remove the sentence 'We also noticed that the guts of L3 escapers were thinner and more fragile at dissection." from the manuscript to avoid subjectivity.
3- They state that Chs2 was able to restore accumulation of chitin in the PM of the proventriculus and the midgut. Please quantify. Additionally, does this restore the morphology of the guts (related to the comment above on the thinner guts in the absence of Chs2)?
We have quantified the rescue of chitin deposition in the PM when Chs2 is expressed in PR cells in a Df(Chs2) mutant background. For this quantification we used the following genetic cross: PRGal4/Cyo; Df(Chs2)/TM6dfdYFP (females) crossed to UASChs2GFP or UASChs2/Cyo; Df(Chs2)/TM6dfdYFP. We selected Df(Chs2) larval escapers by the absence of TM6 (recognisable by the body shape). Among these larval escapers, we identified the presence of Chs2 in PR cells by the expression of GFP or Chs2. We found absence of chitin in the proventriculus and in the midgut in all Df(Chs2) guts that did not express Chs2 in PR cells (n=8/8 Df(Chs2)). In contrast, chitin was present in those intestinal tracts where Chs2 expression was detected in PR cells (n=8/8 PRGal4-UASChs2; Df(Chs2) guts, from 5 independent experiments). The results indicate a full rescue of chitin deposition by Chs2 expression in PR cells in Df(Chs2) mutant larvae. We have added this quantification in the text, chapter 2 (2. Chs2 deposits chitin in the PM).
As requested by the reviewer, we have also conducted measurements to quantify gut thickness. We performed an analysis similar to the one described in point 2, this time comparing the diameter of Df(Chs2) and PRGal4-UASChs2;Df(Chs2) guts at positions 1 and 2 (see image in point 2 of Reviewer 2). Our quantifications indicated that guts were thicker when Chs2 is expressed in the PR region in Df(Chs2) larval escapers.
As discussed in point 2, we have decided not to include these results in the manuscript, as this type of analysis requires a more comprehensive investigation.
Scatter plots quantifying the diameter at the two different positions in Chs2 larval escapers and Chs2 larval escapers expressing Chs2 in PR cells. Bars show mean {plus minus} SD. p=p value of unpaired t test two-tailed with Welch's correction.
4- This may be beyond the scope of this paper, but I find it interesting that the PM chitin is deposited in the proventricular lumen. Yet it forms a thin layer that lines the entire midgut? Any idea how this presumably dense chitin network gets transported throughout the midgut to line the epithelium? I imagine that this is unlikely due to diffusion, especially if they see an even distribution across the midgut. Do they see any evidence of a graded lining (i.e. is it denser in the midgut towards the proventriculus and does this progressively decrease as you look through the midgut?)?
Insect peritrophic matrices have been classified into Type I and II (with some variations) depending on their origin (extensively reviewed in (Peters, 1992, Hegedus et al., 2019). Type I PMs are typically produced by delamination as concentric lamellae along the length of the midgut. Type II PMs, in contrast, are produced in a specialised region of the midgut that corresponds to the proventriculus and are typically more organised than Type I. In Type II PMs, distinct layers originate from distinct cell clusters in the proventriculus. It has been proposed that as food passes, it becomes encased by the extruded PM, which then slides down to ensheath the midgut. Drosophila larvae have been proposed to secrete a type II PM: through PM implantation experiments, Rizki proposed that the proventriculus is required to generate the PM in Drosophila larvae (Rizki, 1956). Our experiments confirmed this hypothesis: we show that expressing Chs2 exclusively in PR cells is sufficient to produce a PM along the midgut. Furthermore, we also show that expressing Chs2 in the midgut is not sufficient to produce a PM layer lining the midgut, at least at larval stages.
The type II PM in Drosophila is proposed to be fully organised into four layers in the proventricular region (also referred as PM formation zone) before reaching the midgut (Peters, 1992, King, 1988, Rizki, 1956, Zhu et al., 2024). However, the mechanism by which the PM is subsequently transported into the midgut remains unclear. PM movement posteriorly is thought to depend on to the pressure exerted by continuous secretion of PM material (Peters, 1992). Early work by Wigglesworth (1929, 1930) proposed that the PM is secreted into the proventricular lumen, becomes fully organised, and is then pushed down by a press mechanism involving the aposed ectodermal/endodermal walls of the proventriculus. Rizki suggested that muscular contractions of the proventriculus walls may play a role, and that peristaltic movements of the gut add a pulling force to push the PM into the midgut (Rizki, 1956). Nevertheless, to our knowledge, the exact mechanism is still not fully understood.
In response to the reviewer's question, the level of resolution of our analysis does not allow us to determine whether there is a graded PM lining along the midgut. However, available data using electron microscopy approaches suggest that the PM is a fully organised structure composed of four layers that is secreted and transported to line the midgut (King, 1988, Zhu et al., 2024).
5- The authors state that expression of kkv in tracheal cells of kkv mutants perfectly restores accumulation of chitin in the luminal filaments. Is this really 100% restoration? They also reference a paper here, which may have quantified this result.
We previously reported that the expression of kkv in tracheal cells restores chitin deposition in kkv mutants (Moussian et al,2015). However, our previous study did not quantify this rescue. As requested by the reviewer, we have now quantified the extent of the rescue.
To perform this quantification, we used the following genetic cross:
btlGa4/(Cyo); kkv/TM6dfdYFP (females) crossed to +/+; kkv UASkkvGFP/TM6dfdYFP (males)
We stained the resulting embryos with CBP (to detect chitin) and GFP. GFP staining allowed us to identify the kkv mutants (by the absence of dfdYFP marker) and to simultaneously identify the embryos that expressed kkvGFP in tracheal cells (through btlGal4-driven expression). Since btlGal4 is homozygous viable, most females carried two copies of btlGal4.
We compared the following embryo populations across 4 independent experiments:
- Cyo/+; kkv/kkv UASkkvGFP (kkv mutants not expressing kkv in the trachea)
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btlGal4/+; kkv/kkv UASkkvGFP (kkv mutants expressing kkv in the trachea) Results:
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Cyo/+; kkv/kkv UASkkvGFP ---- 0/6 embryos deposited chitin in trachea
- btlGal4/+; kkv/kkv UASkkvGFP ---- 27/27 embryos deposited chitin in trachea These results indicate complete restauration of chitin deposition in kkv mutants when kkv is expressed in tracheal cells (100% rescue).
To further investigate whether Chs2 can compensate for kkv function in ectodermal tissues, we performed a similar quantification using the following genetic cross:
btlGa4/(Cyo); kkv/TM6dfdYFP (females) crossed to UASChs2GFP/UASChs2GFP; kkv UASkkvGFP/TM6dfdYFP (males)
We compared the following embryo populations across 2 independent experiments:
- Cyo/UASChs2GFP; kkv/kkv (kkv mutants not expressing Chs2 in the trachea)
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btlGal4/ UASChs2GFP; kkv/kkv (kkv mutants expressing Chs2 in the trachea) Results:
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Cyo/UASChs2GFP; kkv/kkv ---- 0/4 embryos deposited chitin in trachea
- btlGal4/ UASChs2GFP; kkv/kkv ---- 0/16 embryos deposited chitin in trachea These results indicate no restauration of chitin deposition in kkv mutants expressing Chs2 in the trachea (0% rescue).
We have now incorporated these quantifications in the text, chapter 4 (4. Chs2 cannot replace Kkv and deposit chitin in ectodermal tissues.)
6- They ask whether Kkv overexpression in the proventriculus can rescue Chs2 mutants... and vice versa, whether Chs2 overexpression in ectodermal cells can rescue kkv mutants. They show that kkv overexpression leads to an intracellular accumulation of chitin in the proventriculus. However, Chs2 overexpression in the trachea did not lead to any accumulation of chitin in the cells. They tailored their experiments and the associated discussion to address the hypothesis that there is potentially some difference in trafficking of these components. However, another possibility, which they have not ruled out, is that the different ability of kkv and Chs2 to produce chitin inside cells of the proventriculus and ectoderm, respectively, is potentially related to different enzymatic activities and cofactors required for chitin formation in these different cell types. Is this another potential explanation for the differences that they observe?
We note that Kkv overexpression in any cell type (e.g. ectoderm, endoderm) consistently leads to chitin polymerisation. In ectodermal tissues, Kkv expression, in combination with Exp/Reb activity, results in extracellular chitin deposition. In the absence of Exp/Reb, Kkv expression leads to the accumulation of intracellular chitin punctae (De Giorgio et al., 2023, Moussian et al., 2015); this work). This correlates with the accumulation of Kkv at the apical membrane and presence of Kkv-containing vesicles, regardless of the presence of Exp/Reb (De Giorgio et al., 2023, Moussian et al., 2015); Figure 6, S6). In endodermal tissues, regardless of the presence of Exp/Reb, Kkv cannot deposit chitin extracellularly and instead produces intracellular chitin punctae. This correlates with a diffuse accumulation of Kkv in the endodermal cells (PR cells, or gut cells in the embryo) but presence of Kkv-containing vesicles (Figure 6, S6).
In previous work we showed that Kkv's ability to polymerise chitin is completely abolished when it is retained in the ER. Indeed, we found that a mutation in a conserved WGTRE region leads to ER retention, the absence of Kkv-containing vesicles in the cell, and absence of intracellular chitin punctae or chitin deposition (De Giorgio et al., 2023).
These findings indicate a correlation between Kkv subcellular localisation and chitin polymerisation/extrusion. Therefore, we hypothesise that intracellular trafficking and subsequent subcellular localisation play a crucial role in regulating Kkv activity (De Giorgio et al., 2023; this work).
We find that Chs2 is expressed in PR cells (Figure 4) and observe that only in these PR cells does Chs2 localise apically (Fig 5A-D, S5A,B). This localisation correlates with the ability of Chs2 to deposit chitin in the PM and the presence of intracellular chitin punctae in PR cells (Fig 1F). When Chs2 is expressed in other cells types, we detect it primarily in the ER and observed no Chs2-containing vesicles (vesicles are suggestive of trafficking). This localisation correlates with the inability of Chs2 to produce intracellular chitin punctae or extracellular chitin deposition.
Again, these results suggest a correlation between Chs2 subcellular localisation and chitin polymerisation/extrusion, aligning with the results observed for Kkv. Therefore, we hypothesise in this work that the intracellular trafficking and subsequent subcellular localisation of Chs2 play a crucial role in regulating its activity.
Our hypothesis is consistent with seminal work in yeast chitin synthases, which has demonstrated the critical role of intracellular trafficking, and particularly ER exit, in regulating chitin synthase activity (reviewed in (Sanchez and Roncero, 2022).
That said, we cannot exclude other explanations that are also compatible with the observed results. As pointed out by the reviewer, it is possible that Chs2 and Kkv require different enzymatic activities and/or cofactors for chitin polymerisation/deposition, which may be specific to different cell types. Indeed, we know that the auxiliary proteins Exp/Reb are specifically expressed in certain ectodermal tissues (Moussian et al., 2015). These mechanisms could act jointly or in parallel with the regulation of intracellular trafficking, or could even regulate this intracellular trafficking itself.
Identifying the exact mechanisms controlling Kkv and Chs2 intracellular trafficking would be necessary to determine whether additional mechanisms (specific cofactors or enzymatic activities) are also involved or even serve as the primary regulatory elements.
We have introduced these additional possibilities in the discussion section.
7- They co-express Chs2 and Reb and show that this does not lead to chitin production or secretion. In the discussion they conclude that Chs2 does not "seem to be dependent on 'Reb' activity". I think that this statement potentially needs softening. They show that Reb is not sufficient in to induce Chs2 chitin production in cells that do not normally make a PM. However, they do not show that it is not essential in cells that normally express Chs2 and make PM.
We fully agree with the reviewer's observation and thank her/him for pointing it out.
As indicated by the reviewer, we show that co-expression of Reb and Chs2 in different tissues does not lead to an effect distinct from that observed with Chs2 expression alone. In addition, in the discussion we mention that we could not detect expression of reb/exp in PR cells, which aligns with the findings from Zhu et al, 2024, indicating no expression of reb/exp in the midgut cells of the adult proventriculus, as assessed by scRNAseq. We found that exp is expressed in the ectodermal cells of the larval proventriculus (Fig S4D), correlating with kkv expression in this region and cuticle deposition. These findings led us to propose that Chs2 does not seem to be dependent on Exp/Reb activity.
However, in our original manuscript, we did not directly address whether Exp/Reb are required in the cells that normally express Chs2. As a result, we could not conclude that Chs2 relies on a set of auxiliary proteins different from Exp/Reb, and therefore a different molecular mechanism to that of Kkv in regulating chitin deposition.
To address this specific point, we have conducted a new experiment to test Exp/Reb requirement in PR cells. We co-expressed RNAi lines for Exp/Reb in these cells and found that chitin deposition in the PM was not prevented. This further supports the hypothesis that Exp/Reb activity is not necessary for Chs2 function. We have added this experiment to Chapter 4 and Fig S3I,J.
8- They looked at the endogenous expression pattern of kkv and Chs2 and say that they found accumulation of Kkv in the proventriculus and no accumulation in the midgut. Siimilarly, they look at the expression of Chs2 and detect it in cells of the proventriculus. Are there markers of these different cell types that they could use to colocalize these enzymes?
We agree with the reviewer that this is an important issue and we note that Reviewer 1 also raised the same point. Therefore, we have addressed this issue.
We obtained an antibody against Dve, kindly provided by Dr. Hideki Nakagoshi. Dve marks the endodermal region in the proventriculus (Fuss and Hoch, 1998, Fuss et al., 2004, Nakagoshi et al., 1998).This antibody worked nicely in our dissected L3 digestive tracts and allowed us to mark the endodermal region. We also obtained an antibody against Fkh, kindly provided by Dr. Pilar Carrera. Fkh marks the ectodermal foregut cells (Fuss and Hoch, 1998, Fuss et al., 2004, Nakagoshi et al., 1998). While, in our hands, this antibody performed well in embryonic tissues, we observed no staining in our dissected L3 digestive tracts. The reason for this is unclear, but we suspect technical limitations may be responsible (the ectodermal region of the proventriculus is very internal, potentially hindering antibody penetration). To circumvent this inconvenience, we tested a FkhGFP tagged allele available in Bloomington Stock Center. Fortunately, we were able to detect GFP in ectodermal cells of L3 carrying this allele. Using this approach, we conducted experiments to detect Fkh and Dve in relation to chitin accumulation in the wild type (Fig S1). In addition, we used these markers to map the expression of Kkv and Chs2 in the proventriculus (Fig 4). Our results using these endodermal/ectodermal markers confirmed the presence of a cuticle adjacent to the FkhGFP-positive cells and a PM adjacent to the PR cells, marked by Dve. Additionally, we show that Chs2-expressing cells are positive for Dve while Kkv-expressing cells are not. We could not conduct an experiment showing Kkv and Fkh co-expression due to technical incompatibilities, as we have to use GFP tagged alleles for both Kkv and Fkh to reveal their expression. However, we believe that our imaging of Dve/Kkv clearly shows that Kkv expressing cells lack Dve expression and localise in the internal (ectodermal) region of the proventriculus (Fig 4E).
9- They overexpress Chs2 in cells of the midgut and see that it colocalises with an ER marker. They conclude that it is retained in the ER, which again, for them suggests that it has a trafficking problem in these cells. However, they are overexpressing it in these cells and this strong accumulation that they observe in the ER could simply be due to the massive expression levels. Additionally, they cannot conclude that it doesn't get out of the ER at all. They could be correct in thinking that there may be a trafficking issue, but this experiment does not conclusively show that Chs2 is entirely retained in the ER when expressed in ectopic tissues. I wonder if their interpretation needs softening or whether they should potentially address alternative hypotheses.
The reviewer raises two distinct issues: 1) the localisation of overexpressed proteins 2) Chs2 ER retention.
We agree that massive overexpression can lead to artifactual subcellular localisation due to saturation of the secretory pathway, causing ER accumulation. In our experiments, we overexpressed Kkv and Chs2 in different tissues (trachea, salivary glands, embryonic gut, and larval proventriculus), inducing high levels of both chitin synthases.
For Kkv, we observed distinct subcellular localisation patterns in ectodermal versus endodermal tissues (illustrated in new Fig S6). In ectodermal tissues such as the trachea, large amounts of KkvGFP were detected, most of it localising apically. We also detected a more general KkvGFP distribution throughout the cell, including the ER, particularly at early stages. Additionally, we observed many KkvGFP-positive vesicles, reflecting exocytic and endocytic trafficking, as described previously (De Giorgio et al., 2023). The presence of these vesicles (as well as the apical localisation) indicates that KkvGFP is able to exit the ER. Indeed, our previous work demonstrated that when Kkv is retained in the ER, it does not localise apically or appear in vesicles (De Giorgio et al, 2023). In endodermal tissues, as described in our manuscript, KkvGFP did not exhibit polarised apical localisation and instead showed a diffuse pattern with some cortical enrichment. However, the presence of KkvGFP-containing vesicles still suggests that the protein is capable of exiting the ER also in these endodermal tissues.
We observed a different subcellular pattern when we overexpressed Chs2GFP. In tissues where Chs2 is not normally expressed (e.g., trachea, salivary gland, embryonic gut), we did not detect apical or membrane accumulation (see Fig. 5,S5, S6 and response to point 4 of Reviewer #1). Nor did we observe accumulation of Chs2GFP in intracellular vesicles. Instead, Chs2GFP showed strong colocalisation with an ER marker (see Fig. 5,S5, S6 and response to point 4 of Reviewer #1). In contrast, when overexpressed in PR cells, we detected apical enrichment (Fig 5A-D, S5A,B). This indicates that despite massive expression levels, Chs2 can exit the ER in particular tissues.
Taken together, our results strongly suggest that overexpressed Kkv can exit the ER in the different tissues analysed, whereas most Chs2GFP is retained in the ER in tissues other than PR cells. This correlates with the ability of overexpressed KkvGFP to polymerise chitin (either in intracellular puncta or deposited extracellularly depending on the presence of Exp/Reb) in all analysed tissues. Conversely, Chs2 was unable to polymerise chitin (either in intracellular puncta or extracellularly regardless of Exp/Reb presence) in tissues other than PR cells.
Nevertheless, we acknowledge that we cannot definitively conclude that all Chs2 protein is entirely retained in the ER. We have included this caveat in our revised manuscript (Chapter 6 and Discussion section).
Minor Comments: - No mention of Fig 3I in the results section and the order discussed in the results does not match the order in the figure.
We apologise for these inconsistencies. We have addressed this issue in the text, figure legend, and the image order in Figure 3 and Figure S3.
- In the results please provide some information on what the CRIMIC collection is and how it allows you to see Chs2 expression for non-experts.
We have addressed this point in chapter 5 in the revised version, and we now provide a more detailed explanation of the CRIMIC Chs2CR60212-TG4.0 allele.
Further details of this allele are also provided in our responses to points 5 and 9 of Reviewer 1.
Reviewer #2 (Significance (Required)):
Drosophila produce different types of chitinous structures that are required for either the exoskeleton of the animal or for proper gut function (peritrophic matrix). Additionally, most insects have two enzymes involved in the production of chitin and current data suggests that they have unique roles in producing either the exoskeleton or the peritrophic matrix. However, it is unclear whether their different functions are due to differences in cell type expression or differences in physiological activity of the enzymes. The authors exploit Drosophila to drive these 2 enzymes in different cell types that are known to produce the exoskeleton or the peritrophic matrix to determine whether they can functionally substitute mutant backgrounds. Their results give us a hint that these enzymes are not equivalent. What the authors were unable to address is why they are not equivalent. They hypothesise that the different physiological functions of the enzymes may be related to trafficking differences within their respective cell types. While this is an interesting hypothesis, the date are not really clear yet to make this conclusion.
This work will be of interest to anyone interested in chitinous structures in insects and the cell biology of chitin-related enzymes.
Literature
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Author response:
The following is the authors’ response to the original reviews
Public reviews:
Reviewer #1:
The authors attempted to replicate previous work showing that counterconditioning leads to more persistent reduction of threat responses, relative to extinction. They also aimed to examine the neural mechanisms underlying counterconditioning and extinction. They achieved both of these aims and were able to provide some additional information, such as how counterconditioning impacts memory consolidation. Having a better understanding of which neural networks are engaged during counterconditioning may provide novel pharmacological targets to aid in therapies for traumatic memories. It will be interesting to follow up by examining the impact of varying amounts of time between acquisition and counterconditioning phases, to enhance replicability to real-world therapeutic settings.
Major strengths
· This paper is very well written and attempts to comprehensively assess multiple aspects of counterconditioning and extinction processes. For instance, the addition of memory retrieval tests is not core to the primary hypotheses but provides additional mechanistic information on how episodic memory is impacted by counterconditioning. This methodical approach is commonly seen in animal literature, but less so in human studies.
· The Group x Cs-type x Phase repeated measure statistical tests with 'differentials' as outcome variables are quite complex, however, the authors have generally done a good job of teasing out significant F test findings with post hoc tests and presenting the data well visually. It is reassuring that there is a convergence between self-report data on arousal and valence and the pupil dilation response. Skin conductance is a notoriously challenging modality, so it is not too concerning that this was placed in the supplementary materials. Neural responses also occurred in logical regions with regard to reward learning.
· Strong methodology with regards to neuroimaging analysis, and physiological measures.
·The authors are very clear on documenting where there were discrepancies from their pre-registration and providing valid rationales for why.
We thank reviewer 1 for the positive feedback and for pointing out the strengths of our work. We agree that future research should investigate varying times between acquisition and counterconditioning to assess its success in real-life applications.
Major Weaknesses
(1) The statistics showing that counterconditioning prevents differential spontaneous recovery are the weakest p values of the paper (and using one-tailed tests, although this is valid due to directions being pre-hypothesized). This may be due to a relatively small number of participants and some variability in responses. It is difficult to see how many people were included in the final PDR and neuroimaging analyses, with exclusions not clearly documented. Based on Figure 3, there are relatively small numbers in the PDR analyses (n=14 and n=12 in counterconditioning and extinction, respectively). Of these, each group had 4 people with differential PDR results in the opposing direction to the group mean. This perhaps warrants mention as the reported effects may not hold in a subgroup of individuals, which could have clinical implications.
General exclusion criteria are described on page 17. We have added more detailed information on the reasons for exclusion (see page 17). All exclusions were in line with pre-registered criteria. For the analysis, the reviewer is referring to (PDR analysis that investigated whether CC can prevent the spontaneous recovery of differential conditioned threat responses), 18 participants were excluded from this analysis: 2 participants did not show evidence for successful threat acquisition as was already indicated on page 17, and 16 participants were excluded due to (partially) missing data. We now explicitly mention the exclusion of the additional 16 participants on page 7 and have updated Figure 3 to improve visibility of the individual data points. Therefore, for this analysis both experimental groups consisted of 15 participants (total N=30).
It is true that in both groups a few participants show the opposite pattern. Although this may also be due to measurement error, we agree that it is relevant to further investigate this in future studies with larger sample sizes. It will be crucial to identify who will respond to treatments based on the principles of standard extinction or counterconditioning. We have added this point in the discussion on page 14.
Reviewer #2:
Summary:
The present study sets out to examine the impact of counterconditioning (CC) and extinction on conditioned threat responses in humans, particularly looking at neural mechanisms involved in threat memory suppression. By combining behavioral, physiological, and neuroimaging (fMRI) data, the authors aim to provide a clear picture of how CC might engage unique neural circuits and coding dynamics, potentially offering a more robust reduction in threat responses compared to traditional extinction.
Strengths:
One major strength of this work lies in its thoughtful and unique design - integrating subjective, physiological, and neuroimaging measures to capture the various aspects of counterconditioning (CC) in humans. Additionally, the study is centered on a well-motivated hypothesis and the findings have the potential to improve the current understanding of pathways associated with emotional and cognitive control. The data presentation is systematic, and the results on behavioral and physiological measures fit well with the hypothesized outcomes. The neuroimaging results also provide strong support for distinct neural mechanisms underlying CC versus extinction.
We thank reviewer 2 for the feedback and for valuing the thoughtfulness that went into designing the study.
Weaknesses:
(1) Overall, this study is a well-conducted and thought-provoking investigation into counterconditioning, with strong potential to advance our understanding of threat modulation mechanisms. Two main weaknesses concern the scope and decisions regarding analysis choices. First, while the findings are solid, the topic of counterconditioning is relatively niche and may have limited appeal to a broader audience. Expanding the discussion to connect counterconditioning more explicitly to widely studied frameworks in emotional regulation or cognitive control would enhance the paper's accessibility and relevance to a wider range of readers. This broader framing could also underscore the generalizability and broader significance of the results. In addition, detailed steps in the statistical procedures and analysis parameters seem to be missing. This makes it challenging for readers to interpret the results in light of potential limitations given the data modality and/or analysis choices.
In this updated version of the manuscript, we included the notion that extinction has been interpreted as a form of implicit emotion regulation. In addition to our discussion on active coping (avoidance), we believe that our discussion has an important link to the more general framework of emotion regulation, while remaining within the scope of relevance. Please see pages 14 and 15 for the changes. In addition to being informative to theories of emotion regulation, our findings are also highly relevant for forms of psychotherapy that build on principles of counterconditioning (e.g. the use of positive reinforcement in cognitive behavioral therapy), as we point out in the introduction. We believe this relevance shows that counterconditioning is more than a niche topic. In line with the recommendation from reviewer 2, we added more details and explanations to the statistical procedures and analyses where needed (see responses to recommendations).
Reviewer #3:
Summary:
In this manuscript, Wirz et al use neuroimaging (fMRI) to show that counterconditioning produces a longer lasting reduction in fear conditioning relative to extinction and appears to rely on the nucleus accumbens rather than the ventromedial prefrontal cortex. These important findings are supported by convincing evidence and will be of interest to researchers across multiple subfields, including neuroscientists, cognitive theory researchers, and clinicians.
In large part, the authors achieved their aims of giving a qualitative assessment of the behavioural mechanisms of counterconditioning versus extinction, as well as investigating the brain mechanisms. The results support their conclusions and give interesting insights into the psychological and neurobiological mechanisms of the processes that underlie the unlearning, or counteracting, of threat conditioning.
Strengths:
· Mostly clearly written with interesting psychological insights
· Excellent behavioural design, well-controlled and tests for a number of different psychological phenomena (e.g. extinction, recovery, reinstatement, etc).
· Very interesting results regarding the neural mechanisms of each process.
· Good acknowledgement of the limitations of the study.
We thank reviewer 3 for the detailed feedback and suggestions.
Weaknesses:
(1) I think the acquisition data belongs in the main figure, so the reader can discern whether or not there are directional differences prior to CC and extinction training that could account for the differences observed. This is particularly important for the valence data which appears to differ at baseline (supplemental figure 2C).
Since our design is quite complex with a lot of results, we left the fear acquisition results as a successful manipulation check in the Supplementary Information to not overload the reader with information that is not the main focus of this manuscript. If the editor would like us to add the figure to the main text, we are happy to do so. During fear acquisition, both experimental groups showed comparable differential conditioned threat responses as measured by PDRs and SCRs. Subjective valence ratings indeed differed depending on CS category. Importantly, however, the groups only differed with respect to their rating to the CS- category, but not the CS+ category, which suggests that the strength of the acquired fear is similar between the groups. To make sure that these baseline differences cannot account for the differences in valence after CC/Ext, we ran an additional group comparison with differential valence ratings after fear acquisition added as a covariate. Results show that despite the baseline difference, the group difference in valence after CC/Ext is still significant (main effect Group: F<sub>(1,43)</sub>=7.364, p=0.010, η<sup>2</sup>=0.146). We have added this analysis to the manuscript (see page 7).
(2) I was confused in several sections about the chronology of what was done and when. For instance, it appears that individuals went through re-extinction, but this is just called extinction in places.
We understand that the complexity of the design may require a clearer description. We therefore made some changes throughout the manuscript to improve understanding. Figure 1 is very helpful in understanding the design and we therefore refer to that figure more regularly (see pages 6-7). We also added the time between tasks where appropriate (e.g. see page 7). Re-extinction after reinstatement was indeed mentioned once in the manuscript. Given that the reinstatement procedure was not successful (see page 9), we could not investigate re-extinction and it is therefore indeed not relevant to explicitly mention and may cause confusion. We therefore removed it (see page 12).
(3) I was also confused about the data in Figure 3. It appears that the CC group maintained differential pupil dilation during CC, whereas extinction participants didn't, and the authors suggest that this is indicative of the anticipation of reward. Do reward-associated cues typically cause pupil dilation? Is this a general arousal response? If so, does this mean that the CSs become equally arousing over time for the CC group whereas the opposite occurs for the extinction group (i.e. Figure 3, bottom graphs)? It is then further confusing as to why the CC group lose differential responding on the spontaneous recovery test. I'm not sure this was adequately addressed.
Indeed, reward and reward anticipation also evoke an increase in pupil dilation. This was an important reason for including a separate valence-specific response characterization task. Independently from the conditioning task, this task revealed that both threat and reward-anticipation induced strong arousal-related PDRs and SCRs. This was also reflected in the explicit arousal ratings, which were stronger for both the shock-reinforced (negative valence) and reward-reinforced (positive valence) stimuli. Therefore, it is not surprising that reward anticipation leads to stronger PDRs for CS+ (which predict reward) compared to CS- stimuli (which do not predict reward) during CC, but is reduced during extinction due to a decrease in shock anticipation. During the spontaneous recovery test, a return of stronger PDRs for CS+ compared to CS- stimuli in the standard extinction group can only reflect a return of shock anticipation. Importantly, the CC group received no rewards during the spontaneous recovery task and was aware of this, so it is to be expected that the effect is weakened in the CC group. However, CS+ and CS- items were still rated of similar valence and PDRs did not differ between CS+ and CS- items in the CC group, whereas the Ext group rated the CS+ significantly more negative and threat responses to the CS+ did return. It therefore is reasonable to conclude that associating the CS+ with reward helps to prevent a return of threat responses. We have added some clarifications and conclusions to this section on page 8.
(4) I am not sure that the memories tested were truly episodic
In line with previous publications from Dunsmoor et al.[1-4], our task allows for the investigation of memory for elements of a specific episode. In the example of our task, retrieval of a picture probes retrieval of the specific episode, in which the picture was presented. In contrast, fear retrieval relies on the retrieval of the category-threat association, which does not rely on retrieval of these specific episodic elements, but could be semantic in nature, as retrieval takes place at a conceptual level. We have added a small note on what we mean with episodic in this context on page 4. We do agree that we cannot investigate other aspects of episodic memories here, such as context, as this was not manipulated in this experiment.
(5) Twice as many female participants than males
It is indeed unfortunate that there is no equal distribution between female and male participants. Investigating sex differences was not the goal of this study, but we do hope that future studies with the appropriate sample sizes are able to investigate this specifically. We have added this to the limitations of this study on page 17.
(6) No explanation as to why shocks were varied in intensity and how (pseudo-randomly?)
The shock determination procedure is explained on pages 18-19 (Peripheral stimulation). As is common in fear conditioning studies in humans (see references), an ascending staircase procedure was used. The goal of this procedure is to try and equalize the subjective experience of the electrical shocks to be “maximally uncomfortable but not painful”.
Recommendations for the authors:
Reviewer #1:
Very well written. No additional comments
We thank reviewer 1 for valuing our original manuscript version. To further improve the manuscript, we adapted the current version based on the reviewer’s public review (see response to reviewer #1 public review comment 1).
Reviewer #2:
(1) I feel that more justification/explanation is needed on why other regions highly relevant to different aspects of counterconditioning (e.g., threat, memory, reward processing) were not included in the analyses.
We first performed whole-brain analyses to get a general idea of the different neural mechanisms of CC compared to Ext. Clusters revealing significant group differences were then further investigated by means of preregistered ROI analyses. We included regions that have previously been shown to be most relevant for affective processing/threat responding (amygdala), memory (hippocampus), reward processing (NAcc) and regular extinction (vmPFC). We restricted our analyses to these most relevant ROIs as preregistered to prevent inflated or false-positive findings[5]. Beyond these preregistered ROIs, we applied appropriate whole-brain FEW corrections. The activated regions are listed in Supplementary Table 1 and include additional regions that were expected, such as the ACC and insula.
(2) Were there observed differences across participants in the experiment? Any information on variance in the data such as how individual differences might influence these findings would provide a richer understanding of counterconditioning and increase the depth of interpretation for a broad readership.
We agree that investigating individual differences is crucial to gain a better understanding of treatment efficacy in the framework of personalized medicine. Specifically, future research should aim to identify factors that help predict which treatment will be most effective for a particular patient. The results of this study provide a good basis for this, as we could show that the vmPFC in contrast to regular extinction, is not required in CC to improve the retention of safety memory. Therefore, this provides a viable option for patients who are not responding to treatments that rely on the vmPFC. In addition, as noted by Reviewer 1, in both groups a few participants show the opposite pattern (see Figure 3). It will be crucial to identify who will respond to treatments based on the principles of standard extinction or counterconditioning. We have added this point in the discussion on page 14.
(3) While most figures are informative and clear, Figure 3 would benefit from detailed axis labels and a more descriptive caption. Currently, it is challenging to navigate the results presented to support the findings related to differential PDRs. A supplementary figure consolidating key patterns across conditions might also further facilitate understanding of this rather complicated result.
We have made some changes to the figure to improve readability and understanding. Specifically, we changed the figure caption to “Change from last 2 trials CC/Ext to first 2 trials Spontaneous recovery test”, to give more details on what exactly is shown here. We also simplified the x-axis labels to “counterconditioning”, “recovery test” and “extinction”. With the addition of a clearer figure description, we hope to have improved understanding and do not think that another supplemental figure is needed.
(4) Additional details on the statistical tests are needed. For example, please clarify whether p-values reported were corrected across all experimental conditions. Also, it would be helpful for the authors to discuss why for example repeated measures ANOVA or mixed-effects conditions were not used in this study. Might those tests not capture variance across participants' PDRs and SCRs over time better?
We added that significant interactions were followed by Bonferroni-adjusted post-hoc tests where applicable (see page 21). We have used repeated measures ANOVAs to capture early versus late phases of acquisition and CC/extinction, as well as to compare late CC/extinction (last 2 trials) compared to early spontaneous recovery (first 2 trials) as is often done in the literature. A trial-level factor in a small sample would cost too many degrees of freedom and is not expected to provide more information. We have added this information and our reasoning to the methods section on page 21.
Reviewer #3:
(1) Suggest putting acquisition data into the main figures. In fact many of the supplemental figures could be integrated into the main figures in my opinion.
See response to reviewer #3 public review comment 1.
(2) Include explanations for why shock intensity was varied
See response to reviewer #3 public review comment 6.
(3) Include a better explanation for the change in differential responding from training to spontaneous recovery in the CC group (I think the loss of such responding in extinction makes more sense and is supported by the notion of spontaneous recovery, but I'm not sure about the loss in the CC group. There is some evidence from the rodent literature - which I am most familiar with - regarding a loss in contextual gradient across time which could account for some loss in specificity, could it be something like this?).
See response to reviewer #3 public review comment 3.
If we understand the reviewer correctly in that the we see a loss of differential responding due to a generalization to the CS-, this would imply an increase in responding to the CS-, which is not what we see. Our data should therefore be correctly interpreted as a loss of the specific response to the CS+ from the CC phase to the recovery test. Therefore, there is no spontaneous recovery in the CC group, and also not a non-specific recovery. To clarify this we relabeled Figure 3 by indicating “recovery test” instead of “spontaneous recovery”.
(4) Is there a possibility that baseline differences, particularly that in Supplemental Figure 2C, could account for later differences? If differences persist after some transformation (e.g. percentage of baseline responding) this would be convincing to suggest that it doesn't.
See response to reviewer #3 public review comment 1.
(5) As I mentioned, I got confused by the chronology as I read through. Maybe mention early on when reporting the spontaneous recovery results that testing occurred the next day and that participants were undergoing re-extinction when talking about it for the second time.
See response to reviewer #3 public review comment 2.
(6) Page 8 - I was confused as to why it is surprising that the CC group were more aroused than the extinction group, the latter have not had CSs paired with anything with any valence, so doesn't this make sense? Or perhaps I am misunderstanding the results - here in text the authors refer back to Figure 2B, but I'm not sure if this is showing data from the spontaneous recovery test or from CC/extinction. If it is the latter, as the caption suggests, why are the authors referring to it here?
Participants in the CC group showed increased differential self-reported arousal after CC, whereas arousal ratings did not differ between CS+ and CS- items after extinction. We interpret this in line with the valence and PDR results as an indication of reward-induced arousal. At the start of the next day, however, participants from the CC and extinction groups gave comparable ratings. It may therefore be surprising why participants in the CC group do not still show stronger ratings since nothing happened between these two ratings besides a night’s sleep (see design overview in Figure 1A). We removed the “suprisingly” to prevent any confusion.
(7) I suggest that the authors comment on whether there were any gender differences in their results.
See response to reviewer #3 public review comment 5.
(8) The study makes several claims about episodic memory, but how can the authors be sure that the memories they are tapping into are episodic? Episodic has a very specific meaning - a biographical, contextually-based memory, whereas the information being encoded here could be semantic. Perhaps a bit of clarification around this issue could be helpful.
See response to reviewer #3 public review comment 4.
References
(1) Dunsmoor, J. E. & Kroes, M. C. W. Episodic memory and Pavlovian conditioning: ships passing in the night. Curr Opin Behav Sci 26, 32-39 (2019). https://doi.org/10.1016/j.cobeha.2018.09.019
(2) Dunsmoor, J. E. et al. Event segmentation protects emotional memories from competing experiences encoded close in time. Nature Human Behaviour 2, 291-299 (2018). https://doi.org/10.1038/s41562-018-0317-4
(3) Dunsmoor, J. E., Murty, V. P., Clewett, D., Phelps, E. A. & Davachi, L. Tag and capture: how salient experiences target and rescue nearby events in memory. Trends Cogn Sci 26, 782-795 (2022). https://doi.org/10.1016/j.tics.2022.06.009
(4) Dunsmoor, J. E., Murty, V. P., Davachi, L. & Phelps, E. A. Emotional learning selectively and retroactively strengthens memories for related events. Nature 520, 345-348 (2015). https://doi.org/10.1038/nature14106
(5) Gentili, C., Cecchetti, L., Handjaras, G., Lettieri, G. & Cristea, I. A. The case for preregistering all region of interest (ROI) analyses in neuroimaging research. Eur J Neurosci 53, 357-361 (2021). https://doi.org/10.1111/ejn.14954
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Reply to the reviewers
Dear Editor,
Thank you for reviewing our article. We are happy to see that the reviewers are positive on our manuscript. We have tried to address nearly all their comments. Find below a point-by-point answer.
With best regards,
Bruno Lemaitre and Asya Dolgikh
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
This work defines NimB1 protein as a PS binding bridging molecule but with a negative regulatory role in efferocytosis. Specifically, the authors demonstrate via a variety of genetic, cell biological, and other approaches that loss of NimB1 leads to Drosophila macrophages being more adherent to apoptotic targets and engulf them more robustly. The authors also nicely demonstrate that the function of NimB1 differs from NimB4, and the double mutant demonstrating PS-binding yet, distinct roles. Further, the authors show that NimB1 does not affect bacterial phagocytosis.
Overall, this is a well-done study. The authors have already done a very thorough job addressing the key points and I congratulate the authors.
My only minor comment is that the authors could try to make the comment better about whether or not such a 'negative regulatory' bridging molecules may exist in other species, and particularly mammals. If so, this is quite novel. The authors refer to CD47 but this is a membrane protein. The other minor comment is whether the authors ever tried express the PS binding domains as a fusion protein - this would provide a more direct evidence for the binding to PS (although the authors do competitive inhibition with Annexin V). This could be commented upon although testing this is not necessary if they have not already done so.
We greatly appreciate the reviewer’s positive feedback. In the revised manuscript, we have now included a more detailed discussion of mammalian proteins with analogous roles, specifically referencing Draper isoforms (I and II), the CD300 receptor family, and surfactant proteins A and B (see page 16).
Reviewer #1 (Significance (Required)):
The identification of the negative regulator bridging protein NimB1 is novel and could be broadly interesting to those studying efferocytosis.
Regarding the suggestion to overexpress just the putative PS-binding domain of NimB1, we agree this could strengthen the evidence for its PS-binding function. However, generating a new transgenic fly line would require significant additional time. Moreover, the presence of a PS-binding motif was also proposed in the recent study on Orion (Ji et al., 2023), which we have cited in our manuscript. The Orion binds PS through a conserved RRY motif. This motif is critical for Orion’s ability to directly interact with PS and facilitate its secretion. Mutagenesis experiments disrupting the RRY motif—specifically substituting arginine residues with alanines—abolished Orion’s PS-binding capacity, demonstrating the essential role of this sequence. Functional assays also validated that Orion competes with Annexin V, a well-established PS-binding protein, for access to PS-exposing surfaces (Ji et al., 2023).
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Summary:
In this study, Dolgikh and colleagues propose a first investigation about the role of the drosophila Nimrod protein NimB1. Although the role of several members of the family in phagocytosis has been explored, the function of Nimrod type B proteins is less addressed. Within silico analysis, they first see a strong similarity between NimB1 and NimB4. They show that NimB1 is primarily expressed in phagocytes, and as NimB4 can bind phosphatidylserines (PS), leading to a possible shared role in efferocytosis. Using transgenic and null drosophila models, the authors then compare the impact of NimB1 overexpression or deficiency. They compare the effects shown to NimB4 and Draper deficient lines, as these two proteins were previously shown to play a role in efferocytosis. They propose that NimB1 is a secreted protein that binds apoptotic cells. They show that NimB1 deficiency changes the adhesion properties of macrophages. The major finding is that NimB1 delays the early stages of efferocytosis, contrary to NimB4 and Draper that on the contrary facilitate efferocytosis. In contrast, the authors propose that NimB1 increases the formation of phagosomes.
We appreciate the reviewer’s acknowledgment that our key discovery centered around NimB1 functioning as a negative regulator of efferocytosis. This finding highlights NimB1’s distinct role compared to NimB4 and Draper, which instead promote the process.
Major comments:
One of the major technical challenges here was to generate models to allow the detection of the protein in cellulo and in vivo. Although the results are convincing in transgenic lines NimB1 expression is driven by the endogenous promoter, one could still argue that the GFP tags would lead to changes in the localization of the protein.
We understand the concern regarding potential localization changes introduced by GFP tags. However, in previous studies, the same fosmid construct was applied to NimB4-sGFP, and produced a distinctly different expression pattern—NimB4-sGFP expression was more pronounced and clearly present in the glial cells in the brain (Petrignani et al, 2021: Figure EV1A). The fact that the NimB1-sGFP and NimB4-sGFP fosmids localized to different tissues suggests that possible any mis-localization changes due to the GFP tag do not override localization properties intrinsic to the proteins.
In line with the previous comment, to show that NimB1 is a secreted protein, the authors use an overexpression model. How to be sure, that overexpression itself does not lead to increased secretion, or shedding from the membrane?
The observation that uas-NimB1-RFP accumulates in the nephrocytes upon Lpp-Gal4 (fat body) expression, and the presence of a signal peptide suggests that this protein can be secreted.
We cannot exclude that in endogenous condition, NimB1, remains attached to hemocytes. We have confirmed that the Lpp driver is not expressed in nephrocytes.
Would an experiment with a control consisting in a known protein secreted by macrophages lead to the same staining pattern (positive control)? Could another methodology like a Western Blot on supernatants from hemocyte cell culture (over)expressing NimB1, with an anti-RFP staining, be envisaged?
We have already performed similar experiment with other secreted proteins such as NimB4-GFP (Petrignani et al., 2021: Figure: 1B). In the revised article, we have added Viking-RFP as a positive control of a secreted protein (Figure S1F). Figure S2 shows a Western blot with hemolymph extract. We detected NimB1-RFP at its expected molecular weight of 44 kDa, verifying that is present into the hemolymph (Supplementary Document S2 C).
It sems counterintuitive that phagocytes from Draper and NimB4 null mutants with defects in efferocytosis show increased load of apoptotic cells (Figure 6C and D in both unchallenged and injury condition). Do the authors have precedent data to cite going to the same direction? Are cell debris engulfed but not degraded efficiently?
The observation that Draper and NimB4 null mutants have an increased load of apoptotic cells has already been reported in the literature. Several studies have now shown that Draper is not always required for the initial uptake of apoptotic corpses but is critical for phagosome maturation (Meehan et al., 2016; Serizier et al., 2022; Serizier & McCall, 2017). In our article on NimB4 (Petrignani et al., 2021), we have previously shown that the accumulation of immature phagosomes that are not properly eliminated indirectly impairs the uptake of new apoptotic corpses. This explains why efferocytosis is then impaired only at late time points, when unresolved phagosomes have accumulated to the threshold that prevents further phagocytosis.
In Figure 6D it seems indeed that NimB4, NimB1/NimB4 and Draper mutants do not accumulate more apoptotic material upon injury. However, levels for NimB4 is close to the one obtained with NimB1 mutants. Is it statistically true? If yes, what could be the reason for this similarity? In any case, as some important conclusion relies on the comparison between UC and injury conditions, adequate statistics and representations could be proposed.
We thank the reviewer for this pertinent observation and the opportunity to clarify. In the unchallenged (UC) condition, NimB4sk2 and draperΔ5 mutants indeed exhibit significantly elevated levels of apoptotic cell (AC) content in macrophages compared to wild-type and NimB1 mutant genotypes (****p crimic and NimB1229/NimB1crimic* mutants show significantly lower levels in the UC condition, consistent with a role for NimB1 in early recognition or regulation of phagocytic initiation, not in corpse degradation.
In contrast, upon injury (90 minutes post-challenge) we observe a statistically significant increase in apoptotic material in NimB1 mutants compared to UC hemocytes of the same genotype (****p sk2 and draperΔ5* mutants between the UC and 90 min conditions (ns for NimB4). This is consistent with their known defect in corpse degradation, which results in saturation of phagocytic capacity at baseline, and an inability to respond further upon challenge with apoptotic cells.
While the absolute levels of apoptotic material in injured NimB1 and UC NimB4 mutants appear similar at first glance, statistical testing confirms that they are significantly different. NimB4 mutant macrophages retain apoptotic debris due to defective degradation, whereas NimB1 mutants have an increase in newly acquired apoptotic content due to enhanced uptake.
Additionally, NimB161, NimB4sk2 double mutants display a partial increase in apoptotic load upon injury (****p To directly address the reviewer’s suggestion, we have now recalculated and visualized key comparisons with appropriate statistical testing, as shown in Revision Figure 1. All statistical analyses were conducted using unpaired two-tailed Student’s t-tests. This additional figure allows clearer evaluation of genotype-specific differences at both baseline and post-injury conditions and supports our conclusions that NimB1 and NimB4 regulate distinct stages of phagocytosis. We have also clarified the text to better explain that both NimB4 and Draper mutants accumulate unresolved apoptotic material under baseline conditions, and do not accumulate further material upon challenge, due to a block in phagosome maturation.
Revisions Figure 1.
__Quantification of phagocytic events in wild-type and mutant macrophages under unchallenged and post-injury conditions __
(A) Comparison of phagocytic events per frame in w1118 (wild-type), NimB1crimic, NimB1229/NimB1crimic, NimB4sk2, NimB161,NimB4 sk2, and draperΔ5 larvae under unchallenged conditions (UC) and 90 minutes after injury (90 min). Data are presented as individual data points with means. Statistical significance was determined using Student's t-test (*P (B) Direct comparison of phagocytic events between NimB1crimic (red) and NimB4sk2 (gray), and between NimB1229/crimic (dark red) and NimB4sk2 (gray) under both unchallenged (UC) and post-injury (90 min) conditions.
The authors claim with analyses of Figure 8C and D, that NimB1 mutants show acidic vehicles normal in size and fluorescence intensity. However, statistical differences are still observed compared to control condition, which is also seen in representative images shown.
In Figure 8C and D, we provide two quantitative measures to clarify the size and intensity of acidic vesicles. First, we show that mean fluorescence in hemocytes is elevated for all NimB and draper mutants compared to wild type, indicating an overall increase in internalized material. However, we also quantified the number of vesicles per hemocyte and found that NimB1 mutants exhibit significantly more vesicles. Despite this increase, the representative images do not show an obvious enlargement of individual vesicles, suggesting that while more material is being taken up, the vesicles themselves are not enlarged. The enlarged vesicles in case of NimB4 or draper mutant would result from the unresolved cargo (Petrignani et al., 2021). This distinction underscores that higher fluorescence values reflect increased cargo internalization, rather than the larger vesicular structures that result from impaired degradation as in NimB4 or draper mutants.
Minor comments:
In figure 2D, what allows to say the expression is restricted in macrophages? Is it the colocalization with SIMU being a macrophage-specific marker?
In Figure 2D, we relied on SIMU as a macrophage-specific marker in Drosophila embryos to determine that NimB1 expression is restricted to macrophages. Previous research has demonstrated that SIMU is predominantly expressed in embryonic macrophages (where it is essential for apoptotic cell clearance) (Kurant et al., 2008; Roddie et al., 2019). Consequently, the colocalization of NimB1 signal with SIMU-positive cells strongly indicates that NimB1 is confined to macrophages during this developmental stage.
In figure S3B and C, it appears that double NimB1/NimB4 mutants exhibit less spreading than single ones (especially NimB4). Is it the case (statistical significance). If yes what could be the explanation?
Yes, the double NimB1, NimB4 mutants exhibit higher number of hemocytes and significantly reduced cell spreading compared to single mutants. The phenotype is similar to NimC1, eater double mutants (Melcarne et al., 2019) which also show higher number of hemocytes, reduced cell spreading and also diminished capacity to phagocytose apoptotic cells (and, in the case of NimC1, Eater, bacteria as well) (Melcarne et al., 2019). A likely explanation lies in impaired membrane remodeling critical for pseudopod extension and phagosome formation. Studies have shown that defects in actin polymerization or membrane tension can hinder pseudopod extension, reducing phagocytic efficiency (Lee et al., 2007; Masters et al., 2013). Same for the decreased ability of these mutants to form filopodium, a process essential for effective target engagement and engulfment. Filopodia play a significant role in capturing particles and directing them toward the macrophage body for engulfment (Horsthemke et al., 2017). Disruptions in these pathways lead to reduced phagocytic efficiency and a more rounded macrophage morphology, as the cells fail to spread properly (Horsthemke et al., 2017; Lillico et al., 2018). Other than these general observations, we do not have an explanation as to why NimB1, NimB4 double mutants specifically show a higher number of hemocytes and reduced cell spreading.
Several graphs are identical between figure 4 and S4. It is probably not useful and complicates reading.
We agree that duplicating these graphs complicates the presentation. Therefore, we have removed the redundant graphs in the supplementary materials, ensuring the data are shown only once to maintain clarity and ease of reading
As TEM images shown in Figure 8B do not lead to quantitative data, I would put it as supplementary file.
We agree that the TEM images in Figure 8B do not provide strictly quantitative data. To streamline the main manuscript, we have relocated these images to the supplementary section in the revised version
Reviewer #2 (Significance (Required)):
This study uses several approaches and models to address the role of NimB1 in efferocytosis. Both In Vitro and In Vivo approaches are proposed. They give insight into the role of this protein with unknown function so far. Some statistical analysis could be performed to improve the clarity of conclusions. One of the important aspects is the secreted nature of NimB1.However, additional approaches could be proposed to confirm this.
Basic immunologists and cell biologists would be interested in reading this article that highlights the delicate equilibrium between pro and anti-efferocytosis molecules.
I am an immunologist/cell biologist with expertise in lysosomal catabolism. As I work on mouse models or Human samples, my mastering of drosophila as a model is limited.
We thank the reviewer for the positive evaluation of our work. In this revision, we have added further detail to clarify the properties of NimB1 as a secreted protein and strengthen our data presentation. By providing additional clarity on methods and interpretations, we hope immunologists and cell biologists—including those who do not routinely work with Drosophila—will find our findings more accessible.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
This paper investigates the role of NimB1, a secreted member of the Nimrod family in Drosophila, in the process of efferocytosis, the clearance of apoptotic cells by macrophages. Previous studies have identified NimB4, another secreted Nimrod protein, as a positive regulator of efferocytosis, enhancing both apoptotic cell binding and phagosome maturation. In contrast, the authors propose that NimB1 functions as a negative regulator, slowing down the early stages of apoptotic cell binding and internalization. This regulatory balance is suggested to fine-tune efferocytosis to maintain homeostasis.
The primary aim of this study was to characterize the function of NimB1 to better understand the roles of proteins within the NimB family.
This study identifies a novel function for NimB1 in modulating the early stages of efferocytosis, adding to our understanding of how Nimrod proteins fine-tune apoptotic cell clearance. The authors establish a clear phenotypic contrast between NimB1 and NimB4, which provides a compelling framework for understanding how positive and negative regulators coordinate phagocytosis. It also highlights the multiple roles of the secreted members of the Nimrod scavenger receptor family, which have remained so far poorly investigated.
This is an interesting study that could be strengthened by additional validation and broader experimental support. As the authors point out in the discussion, it is known that PS bridging molecules contribute to phagocytosis and that the contribution of positive and negative players finely tune phagocytosis in flies and mammals. Clarifying the mode of action of NimB1 in those processes would higher the impact of this interesting piece of work. For example, does NimB1 interact with NimB4 and if so, what is the role of this interaction? How does NimB1 integrate in the signaling cascade that allows scavenger receptors to bind PS? Does it act similar to Orion by enhancing the PS binding of a scavenger receptor?
Key Findings • NimB1 and NimB4 are structurally similar, as supported by AlphaFold2 modeling, suggesting functional relatedness. • NimB1 is expressed in macrophages, secreted into the hemolymph, and binds apoptotic cells in a phosphatidylserine (PS)-dependent manner. • NimB1 is induced by challenge. • NimB1 mutants display a hyper-phagocytic phenotype, with faster recognition and internalization of apoptotic cells. • NimB1 loss enhances macrophage adhesion and actin remodeling, while bacterial phagocytosis remains unaffected, suggesting a specific role in apoptotic clearance. • NimB1 acts early in the phagocytic process, while NimB4 functions at later stages, particularly in phagosome maturation.
We thank the reviewer for their positive assessment and are pleased that our findings identify NimB1 as a novel secreted negative regulator of efferocytosis, underscoring a greater level of regulatory complexity in apoptotic cell clearance.
Unfortunately, attempts to produce functional NimB1 protein were not successful, limiting our ability to address some of the reviewer’s suggestions experimentally. Despite these challenges, the evidence we present—particularly from our genetic assays—clearly indicates that NimB1 exerts an inhibitory influence during the early steps of apoptotic cell binding, distinguishing it from the late-stage promoting function of NimB4.
Major comments:
Figure 1: AlphaFold is a valuable tool for generating hypotheses, however predicted structures should not be presented as definitive evidence of similarity, particularly without complementary experimental validation. This section would be stronger if the structural predictions were explicitly framed as predictions. In the absence of such data, the interpretation should be toned down.
We agree with the reviewer and we have now framed our observation as prediction and toned down our interpretation. We also note that the similarities between NimB4 and NimB1 are also underlined by the phylogenetic analysis and expression pattern.
Figure 2DE: Given its basal level in homeostatic conditions, it would have been useful to look at the NimB1-GFP upon challenge. Also, the authors show only a single larval macrophage with no comparison point. To strengthen this result, the authors could include another protein quantification method, such as western blotting. Alternatively, labelling of NimB1>UASmRFP in embryo that present the highest expression levels would also strengthen this result.
Unfortunately, we cannot currently perform additional experiments on embryos within the scope of this project because those experiments were performed by our collaborators in Haifa (Estee Kurant Lab). Repeating them would require sending the lines to their lab and accommodating their experimental schedule and manpower constraints.
In supplementary Figure S1F: the authors overexpress NimB1-RFP using the fat body driver Lpp-Gal4 and show larvae with RFP in the nephrocyte. Could filet preparations be shown? Could the authors present evidence that the Lpp driver is not expressed in the nephrocytes (or refer to literature)?
The Lpp-Gal80 driver is described as fat body-specific and has been used to manipulate gene expression in the fat body in many other studies. We have checked Lpp-Gal80>UAS-GFP expression in larvae and did not observe expression in larval nephrocytes. The whole live larvae were observed under the microscope with no prior filet preparations. To provide the evidence that Lpp is not expressed in the nephrocytes we are providing the images of the whole larvae expressing GPF from the Lpp, as per genotype: Lgg-Gal80>UAS-GFP (see below, Revisions Figure 2).
Revisions Figure 2.
__Expression pattern of Lpp-Gal80>UAS-GFP in Drosophila larvae __
Representative fluorescence microscopy images showing GFP expression driven by the Lpp-Gal80 system in Drosophila larvae. The images display dorsal (top) and ventral (bottom) views of the same larva, demonstrating the pattern of expression throughout the fat body tissue. Green fluorescence indicates cells expressing the GFP reporter under the control of the Lpp promoter, which is predominantly active in the larval fat body.
The results on the increased number of hemocytes observed in the double NimB1, NimB4 mutant animals (Figure S3A) remains not only disconnected from the rest of the data but also unexplained. Providing a mechanistic view may require a significant amount of work that may indicate an additional role of the two NimBs but will not add to our understanding of the role of NimB1 in phagocytosis. Nevertheless, it would be at least useful to know whether in the double mutant the lymph gland is still intact, as its precocious histolysis could account for the elevated number of hemocytes. If that were the case, that could indicate that lacking the two NimBs triggers an inflammatory state that affects the lymph gland, meaning that the pathway controlling phagocytosis also has a systemic impact on development. When checking the representative Figure S4D, it seems that very large cells are present in the double mutants, even larger than in the single mutants. These could be (pre)lamellocytes, which constitute activated hemocytes, known to impact the status of the lymph gland. If the enhanced number of hemocytes does not depend on lymph gland histolysis, a simple immunolabeling with the anti-PH3 antibody would assess the proliferative phenotype of the double mutant hemocytes. At least this piece of data would provide a better explanation for the observed phenotype.
We thank the reviewer for this interesting comment. We cannot explain why NimB1, NimB4 double mutants have more hemocytes. It is unclear to us if this is a secondary consequence of defects in efferocytosis or linked to another function of these two NimBs, such as a role in adhesion. We did look at the lymph gland and our preliminary observations suggest that NimB1, NimB4 double mutants have an easily ruptured or fragile lymph gland, which could explain the higher number and the roundish shape of hemocytes in circulation as proposed by the reviewer. Lacking expertise on lymph gland, we prefer not to include this data, as they are not central to the main message of this article on role of NimB1 on efferocytosis. We have also noted the presence of lamellocytes in unchallenged NimB1, NimB4 double mutant larvae, as well as excessive lamellocyte production compared to controls upon clean injury (see below, Revisions Figure 3). We have mentioned the presence of lamellocytes in NimB1, NimB4 double mutants in the revised version. We prefer not include this new data directly in the article because this not central to the main message of the article.
__Revisions Figure 3. __
A.
B.
Lamellocyte recruitment following a clean injury in L3 Drosophila larvae:
(A) Quantification of lamellocytes per 50 frames of x63 microscopy lens in w1118 (wild-type), NimB1crimic, NimB4sk2, NimB161, NimB4sk2, and draperΔ5 larvae under unchallenged conditions (UC) and 3 hours after clean injury (3h). Arrowheads indicate lamellocytes.
(B) Representative confocal microscopy images of hemocytes isolated from challenged NimB161, NimB4sk2 larvae. Cells were fixed and stained with Phalloidin (green) to label F-actin and DAPI (blue) to visualize nuclei. The smaller inset (40x magnification) shows a detailed view of individual lamellocytes with characteristic morphology, while the larger field (20x magnification) displays the overall view on the hemocytes. Scale bar = 50 μm.
Figure 6: The connection between the ex-vivo (Figure 5) and in vivo (Figure 6) assays should be clarified. In the first type of assay, the lack of NimB4 results in reduced internalization (while lack of NimB1 enhances it). In the in vivo assay, more fragments are seen within the cell (hence internalized), using the NimB4 mutant. Also, in the ex-vivo assay, the lack of NimB1 does not affect the first steps ('attachment' and 'membrane'), while NimB4 does, yet it is proposed that NimB1 acts in the early steps (page 11-12). In that case, wouldn't we expect the double mutant NimB1 NmB4 to have the NimB1 phenotype?
The apparent discrepancy between our ex vivo and in vivo assays reflects the different methodologies and what each assay measures. In the ex vivo assay (Figure 4), we add exogenous fluorescently-labeled apoptotic cells to measure new engulfment events. Here, NimB4 mutant macrophages show reduced phagocytic index because they are already saturated with unresolved phagosomes, limiting their capacity to uptake additional corpses, as previously described by (Petrignani et al., 2021). This reduced uptake capacity is reflected in the decreased phagocytic index observed.
In contrast, our in vivo assay (Figure 6) uses DAPI staining to visualize all internalized material, including previously engulfed debris. As expected, we observe accumulation of DAPI signals in NimB4 mutant macrophages under unchallenged conditions, reflecting their inability to process and clear phagosomes rather than enhanced engulfment. This phenotype highlights the role of NimB4 in phagosome maturation rather than initial uptake.
Regarding the role of NimB1 in early phagocytic steps, while attachment and membrane measurements in the ex vivo assay don't show significant differences in NimBcrimic mutants individually, our other experiments demonstrate that NimB1 functions as a negative regulator during early recognition phases. The predominance of the NimB4 phenotype in the NimB1crimic, NimB4 double mutant parallels observations in draper mutants, where double mutants lacking both Draper I (positive regulator) and Draper II (negative regulator) display the Draper I phenotype (Logan et al., 2012). This suggests that phagosome maturation defects (the NimB4 phenotype) present a more severe bottleneck in the phagocytic process than enhanced early uptake (the NimB1crimic phenotype), explaining why the double mutant primarily exhibits accumulation of unresolved phagosomes rather than accelerated uptake. We have re-written this part of the article to clarify these points (see page 11).
Figure 8A: a definition of the phagocytic cup mentioned in the text (page 12, 2nd paragraph) as well as the homogenization of the scale bars in Figure 8A would clarify the interpretation of Figure 8A. The structures shown for w1118 seem quite distant from the structures highlighted for NimB1crimic.
According to reviewer 2, we have now moved this figure to the supplement. The reviewer is correct and we have modified the associated text to clarify the interpretation of the images (see page 12-13).
The same scale should be used across different panels in Figure 8. This is particularly important since the authors mention the size of the lysotracker vesicles to conclude on their levels of maturity. This data and conclusions would be strengthened by a quantification of the vacuole sizes and the combination with markers of phagosome/lysosome maturation levels. It would help disentangling the complementary roles of NimB1 and NimB4.
The scale bar has been homogenized.
Minor comments:
Figure 2BC: is there a particular reason to shift from Rp49 to Rpl32 as normalizing gene in Figure 2B and C? This prevents the comparison of NimB1 expression levels across the different graphs.
We thank the reviewer for highlighting this point. We changed the housekeeping gene from Rp49 to RPL32 in Figure 2C to unify the normalization strategy across all experiments and allow comparisons throughout the manuscript.
Page 9, 2nd paragraph and Figure S3C: the authors mention "Actin structure revealed an increased ratio of filopodia to lamellipodia across all mutants". A clear definition of the parameters defining filopodia and lamellipodia is required to fully appreciate the meaning of the ratio.
We thank the reviewer for the comment. To address this comment, we have included a clear definition of the parameters used to distinguish filopodia and lamellipodia on page 9. In particular, in the revised version we now specify that filopodia were defined as thin, spike-like actin-rich protrusions, while lamellipodia were defined as broad, sheet-like structures at the cell periphery. These criteria were applied consistently for quantification.
Figure S5B: a bar is missing in the right graph (% of cells containing AC, NimB1>UAS-NimB1-RFP). Page 10 2nd paragraph. The authors mention "draper mutants displayed impaired apoptotic cell binding and engulfment" referring to Figure 4. Figure S4 provide a more convincing illustration of this statement, since the decreased phagocytic index in Drpr KO is mostly due to less cells phagocytosing and not less material phagocytosed.
We thank the reviewer for the careful examination. In Figure S5B, the missing bar was due to its color being too close to the background color, making it difficult to distinguish. We have now corrected this by adjusting the color to ensure it is clearly visible.
Regarding the comment on page 10, we agree that Figure S4 more clearly illustrates the impaired apoptotic cell binding and engulfment observed in draper mutants, particularly through the reduced percentage of hemocytes engaging in phagocytosis. We have now clarified the statement in the text to ensure consistency and to guide the reader appropriately to Figure S4 (10).
Figure 6: not easy to distinguish the DAPI labelling relative to the nucleus vs. that of apoptotic fragments.
This is a good point. We have changed the images for clearer demonstration of the DAPI labelling. See Figure 6.
Figure 7B: the number of cells used to generate the violin plot should be indicated in the legend or the method section.
We have mentioned the number of cells used in the quantification (n-50 per genotype) in the figure legend.
A schematic figure recapitulating the data would help
We have added a schematic figure recapitulating the data. See Figure 9 with associated text.
Page 11 last line: homeostatic rather than hemostatic.
Thank you for this comment. We have changed it.
Reviewer #3 (Significance (Required)):
This study identifies a novel function for NimB1 in modulating the early stages of efferocytosis, adding to our understanding of how Nimrod proteins fine-tune apoptotic cell clearance. The authors establish a clear phenotypic contrast between NimB1 and NimB4, which provides a compelling framework for understanding how positive and negative regulators coordinate phagocytosis. It also highlights the multiple roles of the secreted members of the Nimrod scavenger receptor family, which have remained so far poorly investigated.
This is an interesting study that could be strengthened by additional validation and broader experimental support. As the authors point out in the discussion, it is known that PS bridging molecules contribute to phagocytosis and that the contribution of positive and negative players finally tune phagocytosis in flies and mammals. Clarifying the mode of action of NimB1 in those processes would higher the impact of this interesting piece of work. For example, does NimB1 interact with NimB4 and if so, what is the role of this interaction? How does NimB1 integrate in the signaling cascade that allows scavenger receptors to bind PS? Does it act similar to Orion by enhancing the PS binding of a scavenger receptor?
We thank the reviewer for the insightful comments and suggestions. Indeed, understanding the mode of action of NimB1 in the regulation of efferocytosis would significantly strengthen the impact of our findings. Our data, supported by structural and phylogenetic analyses, indicate that NimB1 and NimB4 share a conserved phosphatidylserine (PS)-binding motif, suggesting that these proteins may interact functionally. Preliminary biochemical observations, together with structural predictions, raise the possibility of a direct or indirect interaction between NimB1 and NimB4, although this remains to be experimentally confirmed.
Our observations from NimB1 and NimB4 double mutants reveal that the phenotype closely resembles that of NimB4 single mutants, indicating that NimB4 plays a dominant role in the downstream maturation steps of phagosome processing. These findings are consistent with a model in which NimB1 may modulate early phagocytic uptake, possibly by competing with NimB4 for PS binding or by limiting NimB4 accessibility to apoptotic cells, thereby fine-tuning the rate of efferocytosis.
Regarding the integration into the signaling cascade, while NimB1 and Orion both recognize PS, our data suggest that they function through distinct mechanisms. Orion enhances PS binding to Draper receptor isoforms to promote apoptotic corpse recognition. In contrast, NimB1 appears to act as an inhibitory modulator, potentially masking PS or limiting receptor engagement, thus slowing the phagocytic response. Further functional studies, including receptor-binding assays, will be important to determine whether NimB1 acts by altering receptor-ligand interactions or through a different regulatory pathway.
Future experiments investigating the potential direct interactions between NimB1 and NimB4, their respective affinities for PS, and their influence on phagocytic receptor dynamics will be necessary to better understand NimB1’s precise mode of action. Such studies will help clarify how secreted regulators fine-tune efferocytosis in Drosophila and may offer broader insights into conserved principles of phagocytic regulation across species.
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List of References:
Horsthemke, M., Bachg, A. C., Groll, K., Moyzio, S., Müther, B., Hemkemeyer, S. A., Wedlich-Söldner, R., Sixt, M., Tacke, S., Bähler, M., & Hanley, P. J. (2017). Multiple roles of filopodial dynamics in particle capture and phagocytosis and phenotypes of Cdc42 and Myo10 deletion. The Journal of Biological Chemistry, 292(17), 7258–7273. https://doi.org/10.1074/jbc.M116.766923
Ji, H., Wang, B., Shen, Y., Labib, D., Lei, J., Chen, X., Sapar, M., Boulanger, A., Dura, J.-M., & Han, C. (2023). The Drosophila chemokine–like Orion bridges phosphatidylserine and Draper in phagocytosis of neurons. Proceedings of the National Academy of Sciences, 120(24), e2303392120. https://doi.org/10.1073/pnas.2303392120
Kurant, E., Axelrod, S., Leaman, D., & Gaul, U. (2008). Six-Microns-Under Acts Upstream of Draper in the Glial Phagocytosis of Apoptotic Neurons. Cell, 133(3), 498–509. https://doi.org/10.1016/j.cell.2008.02.052
Lee, W. L., Mason, D., Schreiber, A. D., & Grinstein, S. (2007). Quantitative Analysis of Membrane Remodeling at the Phagocytic Cup. Molecular Biology of the Cell, 18(8), 2883–2892. https://doi.org/10.1091/mbc.E06-05-0450
Lillico, D. M. E., Pemberton, J. G., & Stafford, J. L. (2018). Selective Regulation of Cytoskeletal Dynamics and Filopodia Formation by Teleost Leukocyte Immune-Type Receptors Differentially Contributes to Target Capture During the Phagocytic Process. Frontiers in Immunology, 9. https://doi.org/10.3389/fimmu.2018.01144
Masters, T. A., Pontes, B., Viasnoff, V., Li, Y., & Gauthier, N. C. (2013). Plasma membrane tension orchestrates membrane trafficking, cytoskeletal remodeling, and biochemical signaling during phagocytosis. Proceedings of the National Academy of Sciences, 110(29), 11875–11880. https://doi.org/10.1073/pnas.1301766110
Meehan, T. L., Joudi, T. F., Timmons, A. K., Taylor, J. D., Habib, C. S., Peterson, J. S., Emmanuel, S., Franc, N. C., & McCall, K. (2016). Components of the Engulfment Machinery Have Distinct Roles in Corpse Processing. PLOS ONE, 11(6), e0158217. https://doi.org/10.1371/journal.pone.0158217
Melcarne, C., Ramond, E., Dudzic, J., Bretscher, A. J., Kurucz, É., Andó, I., & Lemaitre, B. (2019). Two Nimrod receptors, NimC1 and Eater, synergistically contribute to bacterial phagocytosis in Drosophila melanogaster. The FEBS Journal, 286(14), 2670–2691. https://doi.org/10.1111/febs.14857
Petrignani, B., Rommelaere, S., Hakim-Mishnaevski, K., Masson, F., Ramond, E., Hilu-Dadia, R., Poidevin, M., Kondo, S., Kurant, E., & Lemaitre, B. (2021). A secreted factor NimrodB4 promotes the elimination of apoptotic corpses by phagocytes in Drosophila. EMBO Reports, 22(9), e52262. https://doi.org/10.15252/embr.202052262
Roddie, H. G., Armitage, E. L., Coates, J. A., Johnston, S. A., & Evans, I. R. (2019). Simu-dependent clearance of dying cells regulates macrophage function and inflammation resolution. PLoS Biology, 17(5), e2006741. https://doi.org/10.1371/journal.pbio.2006741
Serizier, S. B., & McCall, K. (2017). Scrambled Eggs: Apoptotic Cell Clearance by Non-Professional Phagocytes in the Drosophila Ovary. Frontiers in Immunology, 8, 1642. https://doi.org/10.3389/fimmu.2017.01642
Serizier, S. B., Peterson, J. S., & McCall, K. (2022). Non-autonomous cell death induced by the Draper phagocytosis receptor requires signaling through the JNK and SRC pathways. Journal of Cell Science, 135(20), jcs250134. https://doi.org/10.1242/jcs.250134
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link.springer.com link.springer.com
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Once multiple accurate students enter the same tag for a new image, the system wouldbe confident that the tag is correct. In this manner, image tagging and vocabulary learning can becombined into a single activity.
is this not how CAPTCHA is evaluated too?
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stackoverflow.com stackoverflow.com
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There is recent update that enables such functionality - https://github.com/moby/buildkit/releases/tag/dockerfile/1.7.0-labs To work with it - add comment in the beginning of the Dockerfile # syntax=docker.io/docker/dockerfile:1.7-labs
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- Apr 2025
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github.com github.com
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Allow you to save files from apps to any folder in drive
That is quite something
How would the code look like
I am using "STORE_APP_DATA" permission so I can pass any path?
Will try it straight away
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stackoverflow.com stackoverflow.com
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annotated tags point to a tag object in the object database. git tag -as -m msg annot cat .git/refs/tags/annot contains the SHA of the annotated tag object: c1d7720e99f9dd1d1c8aee625fd6ce09b3a81fef and then we can get its content with: git cat-file -p c1d7720e99f9dd1d1c8aee625fd6ce09b3a81fef
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social-media-ethics-automation.github.io social-media-ethics-automation.github.io
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We might want to avoid physical danger from a stalker, so we might keep our location private
Keeping information private is vital but it is specifically interesting to see that having our location be private be interesting. I mention this as many of the people I know around me post where they are and tag their locations and have their social media accounts open to the public rather than having it private and closed only to their friends. People I believe do not realize how much they are exposing themselves by constantly posting their current or past locations on the internet which can later have issues be exposed (if they are like public figures) and have people attack them.
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www.biorxiv.org www.biorxiv.org
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Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.
Learn more at Review Commons
Reply to the reviewers
We thank the reviewers for their thoughtful comments and suggestions. Our plans for revisions are first summarized. Below you can find the original reviews and our responses and detailed plans (indicated by "Response").
Revision plan summary:
- Many of the concerns can be addressed by changes in the text and better explanations of how the experiments were done. These changes are detailed in the point-by-point responses.
- The reviewers suggested experiments such as ChIP-seq and immunoprecipitation which require collection of a large number of mutants. Since our mutants are sterile, the line needs to be maintained as heterozygotes, from which we can pick out individual mutant worms. Therefore, with the current reagents it is impossible to collect mutants in sufficient quantities for ChIP-seq or IP. We understand that it limits the conclusions that can be drawn.
- For some figures, additional quantification of fluorescence signal will be done to show differences between mutant and wild type.
- A few experiments will be repeated:
- We will repeat the ATPase assays shown on Fig 1 with additional independently prepared and purified protein samples.
- Additional replicates will be performed for the few immunofluorescence experiments that were only performed once. Point-by-point responses:
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
Dosage compensation (DC) in C. elegans involves halving the gene expression from the two hermaphrodite X chromosomes to match the output of the single X in male worms. The key regulator of this repression is a specialized condensin complex, which is defined by a dedicated SMC-4 paralog, termed DPY-27. SMC-4 in other animals is an ATPase that functions as a motor of loop extrusion in cohesion complexes. In their current manuscript, Chawla et al. assessed whether DPY-27 has ATPase function and whether this activity is required for dosage compensation. It had previously been shown that an ATPase-deficient 'EQ' mutant DPY-27 protein interacts with other DC complex members, yet fails to localize to the X. This observation was made with an extra copy of DPY-GFP expressed in addition to the endogenous wildtype protein [Ref 77]. No dominant negative effect was observed. The authors have now engineered the 'EQ' mutation into the endogenous gene locus and genetically generated hetero- and homozygous ATPase mutant worms. Their data suggest that the ATPase activity is required or X-chromosome localization, complex assembly, chromosome compaction as well as enrichment of H4K20me1 on the dampened X chromosome.
Major comments: 1. ATPase assays, Figure 1.Preparations of individual recombinant proteins may vary significantly and may occasionally show much reduced enzymatic activity. A conclusion about the failure of an ATPase activity should not be concluded from a single preparation, but several protein preps need to be tested, which then serve as 'biological replicates' for the in vitro reaction. Apparently, the ATPase assays shown only involved technical replicates, which is not sufficient.
Response: We will express and purify additional protein samples and will repeat the assay.
CRISPR-mediated engineering may lead to unwanted reactions, exemplified by the 'indel' mutation that was recovered in one clone. As a good practice and important control, the sequences of the mutated alleles in the worms should be determined by sequencing of PCR products. Restrictions enzyme cleavage or gel electrophoresis of the PCR products is not sufficient to document the nature of the mutation.
Response: The sequence of the edit was confirmed by Sanger sequencing. We will make it clear in the text.
All IF data need to be collected from at least 2 biological replicates, i.e. the experiment must have been carried out independently on two different days. The replicates should deliver consistent results. The number of independent replicates should be mentioned in each figure legend.
Response: Most of our experiments were performed multiple times. We will indicate the number of replicates in the figure legends. The one or two experiments that were only performed once, will be repeated an additional time.
The expression levels of wildtype and mutant proteins are concluded from IFM. This is very qualitative; quantitative measurements would strengthen the paper.
Response: We will quantify fluorescence intensity on our existing images to show differences between mutant and wild type.
Figure 4B: What are the criteria for classification of the three classes of mutant nuclei? To the uninitiated eye they look very similar. I am a bit worried about the human bias, if such diffuse staining are to be categorized. The two categories of localization need be documented better.
Response: We will provide more images to show the range of phenotypes and provide a better explanation of how they were classified. We will also try a few ways to quantify “diffuseness” to provide a numerical readout.
Figure 5: volume of the X chromosome. Related to (5): Apparently, the mask that contains the X chromosome was drawn by hand on each individual nucleus? I find it very difficult to see how the X chromosomal territory would be assessed in the examples shown. I would be good to see a panel of nuclei, in which the masks are visible. I think the analysis should be blinded, in which a researcher not involved in the analysis draws masks on coded nuclei and their classes are only revealed later. The same concern holds for the FISH/IP overlaps or DPY-27/SDC-2 overlaps.
Response: The masks used were not drawn by hand but were based on fluorescence intensity thresholds. We will make a supplementary figure that shows the masks used for quantification to help clarify how the experiment and quantification were performed.
For figure 5, age-matched hermaphrodites were analyzed. How was the age determined and what would be the consequence of age-variations? What is the effect of the mutations on development?
Response: For our staining experiments, we routinely use young adult which we define as 24 hr past larval L4 stage. At this stage, young adults have started laying eggs. We have unpublished data that shows that dosage compensation and chromosome compaction deteriorates with age. To avoid using old worms in our assays, we pick L4 larvae, and then use them for experiments the following day.
Minor comments: 8. The labeling of p-values as a-f in the figures with the values listed in a supplemental table is not comfortable. The p-values corresponding to the letters should be listed in the corresponding legends.
Response: p values can be added to the figure or the figure legend (they are currently in supplementary tables).
How were the concentrations of the ATPase preparations determined? It would help to see a proteins gel in the supplement to assess their purity.
Response: Concentrations were determined using a spectrometer. We can show protein gels of the preparations as a supplementary figure.
In figure 1, heterodimers are assumed, but not shown. Do they dimerize under these conditions?
Response: We can cite papers from others that show heterodimerization in these conditions (for example, Hassler et al, 2019).
Reviewer #1 (Significance (Required)):
Significance: The involvement of the ATPase function of DPY-27 was somewhat expected, in light of the earlier findings published in reference 77 using a transgene. The current study confirms and extends these earlier findings. In principle, the genetic experiment presented here is stronger, if documented better.
Strengths: The study investigates endogenous proteins and measures different phenomena known to be correlated from previous work. The data are internally consistent.
Limitations: The lack of biological replicates, and unclear procedures of how to draw the IF masks that underlie the conclusions about X chromosome (co)localization and nuclear volume determination render the argument less convincing. For this reviewer, who is not in the C. elegans field, the analysis of mutant phenotypes is difficult to follow. The conclusions are based on only one type of experiment. In reference 77, the X chromosome binding was done by ChIP-seq, clearly a superior, complementary method.
Response: As explained above, since the strain has to be maintained as a heterozygote, we are unable to collect enough mutants for a ChIP-seq experiment. We can perform and better document the experimental replicates and we can better explain the quantification methods used.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Summary: The authors analyzed the ATPase function of an SMC-4 variant required for dosage compensation in C. elegans. They made a single amino acid mutation that significantly reduced ATPase activity of the protein as shown by in vitro ATP hydrolysis. They showed that the mutation results in the phenotypic consequences of those shown for other DC mutants, including viability assay, immunofluorescence and DNA FISH. These results demonstrate the important role of ATPase activity in transcription repression.
Major comments: - Are the key conclusions convincing? The key conclusion that DPY-27 has ATPase activity and using a classic mutation that reduces it largely eliminates its function is convincing. The interpretation of the IF experiments to build the model in the final figure requires stronger evidence, as commented below in additional experiment section.
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Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? Yes, as explained below.
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Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.
The main issue with the current model is that the authors assume that the EQ proteins that they are analyzing is in complex with the rest of the condensin IDC subunits. However, there is no evidence in the paper suggesting that this occurs. The results are consistent with the possibility that a large portion of the DPY27-EQ is not in a complex.
IP-western experiments comparing the proportion of other subunits pulled down by the wild type versus the EQ mutant (perhaps extract from ~50% EQ containing population could be reached) is needed to understand the incorporation of the EQ mutant in the complex. This is particularly important for the interpretation of the data in Figure 4A, where 70% of the nuclei show diffuse CAPG-1 and DPY-27 EQ. Is this signal due to disassembled subunits diffusing freely, or as depicted in the model figure, bound less stably everywhere? The immunofluorescence results are consistent with both EQ mutation 1) forming a full complex and unstably binding or 2) destabilizing the complex but incompletely assembled complexes sustaining a pool of free EQ detected by the immunofluorescence experiments.
Response: We agree that to conclusively show interactions, an IP would be necessary. However, as explained above for ChIP, it is not possible to collect enough mutants to make enough protein extract for an IP. An IP in heterozygous worms is also not ideal, as it would be nearly impossible to distinguish wild protein from the mutant. The antibody we used recognizes the N terminus, which is identical in the two proteins. The only way to distinguish them would be mass spec. However, during the fragmentation process for mass spec, Q can deaminate to E, which would complicate interpretation of our data. To do this experiment properly, we would need to introduce a different tag into the mutant protein. With the current reagents, an IP is not possible.
Instead, we have to rely on indirect evidence. The fact that DPY-27 and CAPG-1 colocalize (figure 4) does provide some support for the hypothesis. From previous studies,including our recent publication Trombley et al PLoS Genetics 2025, we know that the condensin IDC complex is not stable unless all subunits are present. It is therefore highly unlikely, although not impossible, that what we detect is diffuse individual subunits.
We can make changes in the text to soften this claim and better discuss the caveats of the experiment and the conclusions.
Along the same point, authors show that EQ protein that binds to the X is incapable of bringing H4K20me1, which is consistent with the possibility that a large portion of the EQ protein is not in a complex. : "To our surprise, we observed that there was no discernable enrichment of H4K20me1, even though there is discernable enrichment of DPY-27 EQ on the X chromosomes in the dpy-27 EQ mutants (Figure 8A).
Response: There is an important difference. CAPG-1 and DPY-27 are both members of condensin IDC. The five subunits of this complex depend on each other for stability. DPY-21, the protein that introduces the H4K20me1 mark, also localizes to the X chromosomes, but is not part of condensin IDC. Condensin IDC is able to localize to the X chromosomes in the absence of DPY-21, and is not dependent on DPY-21 for stability. However, DPY-21 is dependent on condensin IDC for X localization (Yonker et al 2003). It is then possible that the mutant condensin IDC is X-bound, but it is unable to recruit DPY-21. We can clarify this in the text.
- Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments. It is unclear how long it would take to collect enough het/mutant worms can be collected for IP-western. Without additional evidence, interpretation of the data would be affected.
Response: As explained above, collecting enough mutant worms is essentially impossible. Collecting enough heterozygotes is possible, but distinguishing the mutant protein from the wild type in hets is not.
- Are the data and the methods presented in such a way that they can be reproduced? Yes
- Are the experiments adequately replicated and statistical analysis adequate? Yes, except the presentation of the test (see minor comment below)
Minor comments: - Specific experimental issues that are easily addressable. The use of letters for statistical test result is confusing and the figure legend is not clear about what actual p values were produced "Letters represent multiple comparison p values, with different letters indicating statistically significant differences, and any repeated letter demonstrating no significance. " Providing the values at a reasonably concise manner in the legend will help the reader a lot.
Response: P values can be added to the figures, or the legend
- Are prior studies referenced appropriately? The authors state that "Surprisingly, this mutant did not phenocopy the transgenic EQ mutant in [77], .." however in the previous paragraph, the authors state that the transgenic was expressed in the presence of wild type copy. Therefore, the endogenous mutant showing phenotypes rather than the transgenic is rather expected.
Response: What we referred to were ways in which the protein behaved (for example in ability to bind to the X at all), and not mutant phenotypes of worms. We can clarify this in the text.
The authors state that "One possible explanation could be that mitotic condensation has multiple drivers of equal consequence including changes in histone modifications [129], whereas condensation of dosage compensated X chromosomes is predominantly dependent on the DCC. " In a dpy-21 mutant, X chromosome decondenses but DPY-27 stays on the chromosome. Therefore, the effect of the EQ mutation may be due to lack of H4K20me1 enrichment in addition to the lack of loop extrusion.
Response: We can add the role of H4K20me1 to the discussion.
- Are the text and figures clear and accurate? Yes
- Do you have suggestions that would help the authors improve the presentation of their data and conclusions? The Pearson correlation coefficient for assessing colocalization between SDC-2 and DPY-27 was helpful for quantification, because there is a lot of background signal that makes the support for or lack of colocalization with the X in the other IF/FISH figures difficult to assess. Additionally, please provide information on how chromatic aberration was assessed when analyzing colocalization experiments.
Response: Chromatic aberration was not considered for these experiments.
Reviewer #2 (Significance (Required)):
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Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. Although long assumed to be a functional SMC, the demonstration of DPY-27 function depending on ATPase activity is important. This demonstrates that an X-specific condensin retained its SMC activity.
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Place the work in the context of the existing literature (provide references, where appropriate). The authors do an adequate job in doing this in their discussion.
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State what audience might be interested in and influenced by the reported findings. The field of 3D genome organization and function would be influenced by the reported findings.
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Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.
Genomic analyses of 3D genome organization and gene expression.
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172.16.212.25:2222 172.16.212.25:2222
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ext to emphasize th
I give some URL here as a reference.
@parvinnabili testing tag. Please disregard.
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www.biorxiv.org www.biorxiv.org
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Reviewer #2 (Public review):
Summary:
In this manuscript, the authors investigated how the type-I interferon response (ISG) and antigen presentation (AP) pathways are repressed in luminal breast cancer cells and how this repression can be overcome. They found that a STING agonist can reactivate these pathways in breast cancer cells, but it also does so in normal cells, suggesting that this is not a good way to create a therapeutic window. Depletion of ADAR and inhibition of KDM5 also activate ISG and AP genes. The activation of ISG and AP genes is dependent on cGAS/STING and the JAK kinase. Interestingly, although both ADAR depletion and KDM5 inhibition activate ISG and AP genes, their effects on cell fitness are different. Furthermore, KDM5 inhibitor selectively activates ISG and AP genes in tumor cells but not normal cells, arguing that it may create a larger therapeutic window than the STING agonist. These results also suggest that KDM5 inhibition may activate ISG and AP genes in a way different from ADAR loss, and this process may affect tumor cell fitness independently of the activation of ISG and AP genes.
The authors further showed that KDM5 inhibition increases R-loops and DNA damage in tumor cells, and XPF, a nuclease that cuts R-loops, is required for the activation of ISG and AP genes. Using H3K4me3 CUT&RUN, they found that KMD5 inhibition results in increased H3K4me3 not only at genes, but also at repetitive elements including SINE, LINE, LTR, telomeres, and centromeres. Using S9.6 CUT&TAG, they confirmed that R-loops are increased at SINE, LINE, and LTR repeated with increased H3K4me3. Together, the results of this study suggest that KMD5 inhibition leads to H3K4me3 and R-loop accumulation in repetitive elements, which induces DNA damage and cGAS/STING activation and subsequently activates AP genes. This provides an exciting approach to stimulate the anti-tumor immunity against breast tumors.
KDM5 inhibition activates interferon and antigen presentation genes through R-loops.
Strengths:
Overall, this study was carefully designed and executed. This is a new approach to make breast tumors "hot" for anti-tumor immunity.
Weaknesses:
Future in vivo studies are needed to show the effects of KDM5 inhibitors on the immunotherapy responses of breast tumors.
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social-media-ethics-automation.github.io social-media-ethics-automation.github.io
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Have you witnessed different responses to trolling? What happened in those cases? What do you think is the best way to deal with trolling?
I have witnessed trolling. I think in a day where social media is so popular trolling has become normalized because individuals can hide behind a username to make a comment about someone. Most trolling cases I see are with celebrities online because they have a large preseence and garner attention from trolls because of their following. Trolls will comment on their lifestyle choices in the comments of their posts or tag them in a video saying awful things about the individual. I think a good example of celebrities being trolled recently is a Blake Lively-Justin Baldoni drama. I agree with the rules of internet protocol to ignor trolls. Responding gives them attention which gives the trolls more power.
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social-media-ethics-automation.github.io social-media-ethics-automation.github.io
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If the immediate goal of the action of trolling is to cause disruption or provoke emotional reactions, what is it that makes people want to do this disruption or provoking of emotional reactions? Some reasons people engage in trolling behavior include: Amusement: Trolls often find the posts amusing, whether due to the disruption or emotional reaction. If the motivation is amusement at causing others’ pain, that is called doing it for the lulz [g6]. Gatekeeping: Some trolling is done in a community to separate out an ingroup from outgroup (sometimes called newbies or normies). The ingroup knows that a post is just trolling, but the outgroup is not aware and will engage earnestly. This is sometimes known as trolling the newbies. Feeling Smart: Going with the gatekeeping role above, trolling can make a troll or observer feel smarter than others, since they are able to see that it is trolling while others don’t realize it. Feeling Powerful: Trolling sometimes gives trolls a feeling of empowerment when they successfully cause disruption or cause pain.** Advance and argument / make a point: Trolling is sometimes done in order to advance an argument or make a point. For example, proving that supposedly reliable news sources are gullible by getting them to repeat an absurd gross story [g5]. Punish or stop: Some trolling is in service of some view of justice, where a person, group or organization is viewed as doing something “bad” or “deserving” of punishment, and trolling is a way of fighting back.
I have always encountered such "trolling" online, some are for amusement purposes, but I felt like they have more kind than malice. Besides that, I believe it is also a way of gatekeeping, but as people "tag" their post, such gatekeeping post will only be pushed to the "ingroup" people.
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learn.cantrill.io learn.cantrill.io
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Welcome back, and in this video, I want to talk in general about application layer firewalls, also known as layer 7 firewalls, named after the layer of the OSI model that they operate at. I want to keep this video pretty generic and will talk about how AWS implements this within their product set in a separate video. So let's just jump in and get started.
Before I talk about the high-level architecture and features of layer 7 firewalls, let's quickly refresh our knowledge of layers 3, 4, and 5. We start with a layer 3 and 4 firewall, which is helping to secure the Categorum application—now accessed by millions of people globally because it's that amazing. Because this is a layer 3 and 4 firewall, it sees packets and segments, IP addresses, and ports. It sees two flows of communication: requests from the laptop to the server, and then responses from the server back to the laptop. However, because this firewall is limited to layers 3 and 4 only, these are viewed as separate and unrelated streams of data—request and response—even though they’re part of the same communication from a human perspective.
If we enhance the firewall by adding session capability, then the same communication between the laptop and server can be viewed as one. The firewall understands that the request and the response are part of the same session. This small difference reduces administrative overhead—allowing for one rule instead of two—and also lets you implement more contextual security, where you can treat response traffic in the context that it’s a response to an original request, rather than just arbitrary traffic in the same direction.
Now, this next point is really important: in both cases, these firewalls don't understand anything above the layer at which they operate. The top firewall operates at layers 3 and 4, so it understands layers 1 through 4. The bottom firewall does this as well but additionally understands layer 5. What this means is that both firewalls can see IP addresses, ports, and flags, and the bottom one can also understand sessions. However, neither of them can understand the data that flows above this—they have no visibility into layer 7, such as HTTP. They can't see headers or any other data transferred over HTTP. To them, layer 7 traffic is opaque—a cat image is the same as a dog image or malware—and this is a significant limitation that exposes the systems we're protecting to a wide range of attacks.
Layer 7 firewalls fix many of these limitations. Let’s consider the same architecture: a client on the left and a server or application on the right that we’re trying to protect. In the middle, we have a layer 7 firewall, and to help remember it, let’s add a smart robot to represent its capabilities. With this firewall, we still have the same flow of packets and segments, and a layer 7 firewall can understand all the lower layers—but it adds additional capabilities.
Consider this example where the Categor application is connected using an HTTPS connection, which is encrypted HTTP, and HTTP is the layer 7 protocol. The first important thing to realize is that layer 7 firewalls understand various layer 7 protocols. In this example, we're focusing on HTTP, so the firewall understands how that protocol transfers data: its architecture, headers, data, hosts, and all other components happening at or below layer 7. This means it can identify normal or abnormal elements of a layer 7 connection and protect against various protocol-specific attacks or weaknesses.
In the HTTPS connection to the Categor server, the HTTPS connection would be terminated at the layer 7 firewall. While the client believes it is connecting directly to the server, the firewall strips away the HTTPS tunnel, leaving plain HTTP, which it can analyze. Then, a new HTTPS connection is created between the layer 7 firewall and the backend server. From the server and client perspectives, this process is transparent. The crucial part is that, between the original and the new HTTPS connections, the firewall sees the unencrypted HTTP traffic in plain text. Because the firewall understands the layer 7 protocol, it can inspect, block, replace, or tag the data within that protocol stream.
This inspection might involve protecting the integrity of the Categor application by logically allowing cat pictures while rejecting dog images or labeling sheep images as spam. You might choose to be inclusive and only block truly dangerous content such as malware or exploits. Because the firewall understands one or more application protocols, you can allow or block content with great precision. You can even replace content—for instance, adult images might be replaced with kitten pictures or baby animals. Moreover, you can block specific applications like Facebook or prevent business data from being uploaded to services such as Dropbox.
The key thing to understand is that a layer 7 firewall retains all the capabilities of layers 3, 4, and 5 firewalls, but adds the ability to react to layer 7 elements. This includes DNS names, connection rates, content, headers—anything that exists in the specific layer 7 protocol that the firewall understands. Some layer 7 firewalls only support HTTP, while others might support SMTP, the protocol used for email delivery. The limit is defined only by what the firewall software is built to handle.
That’s everything I wanted to cover at a high level. Coming up in future videos, I’ll discuss how AWS implements layer 7 firewall capability within its product set. For now, though, this high-level understanding is the main focus of this video. So go ahead and complete the video, and when you're ready, I’ll look forward to you joining me in the next.
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www.biorxiv.org www.biorxiv.org
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Author response:
Reviewer #1 (Evidence, reproducibility and clarity):
Authors has provided a mechanism by which how presence of truncated P53 can inactivate function of full length P53 protein. Authors proposed this happens by sequestration of full length P53 by truncated P53.
In the study, performed experiments are well described.
My area of expertise is molecular biology/gene expression, and I have tried to provide suggestions on my area of expertise. The study has been done mainly with overexpression system and I have included few comments which I can think can be helpful to understand effect of truncated P53 on endogenous wild type full length protein. Performing experiments on these lines will add value to the observation according to this reviewer.
Major comments:
(1) What happens to endogenous wild type full length P53 in the context of mutant/truncated isoforms, that is not clear. Using a P53 antibody which can detect endogenous wild type P53, can authors check if endogenous full length P53 protein is also aggregated as well? It is hard to differentiate if aggregation of full length P53 happens only in overexpression scenario, where lot more both of such proteins are expressed. In normal physiological condition P53 expression is usually low, tightly controlled and its expression get induced in altered cellular condition such as during DNA damage. So, it is important to understand the physiological relevance of such aggregation, which could be possible if authors could investigate effect on endogenous full length P53 following overexpression of mutant isoforms.
Thank you very much for your insightful comments.
(1) To address “what happens to endogenous wild-type full-length P53 in the context of mutant/truncated isoforms," we employed a human A549 cell line expressing endogenous wild-type p53 under DNA damage conditions such as an etoposide treatment(1). We choose the A549 cell line since similar to H1299, it is a lung cancer cell line (www.atcc.org). For comparison, we also transfected the cells with 2 μg of V5-tagged plasmids encoding FLp53 and its isoforms Δ133p53 and Δ160p53. As shown in Author response image 1A, lanes 1 and 2, endogenous p53 expression, remained undetectable in A549 cells despite etoposide treatment, which limits our ability to assess the effects of the isoforms on the endogenous wild-type FLp53. We could, however, detect the V5-tagged FLp53 expressed from the plasmid using anti-V5 (rabbit) as well as with antiDO-1 (mouse) antibody (Author response image 1). The latter detects both endogenous wildtype p53 and the V5-tagged FLp53 since the antibody epitope is within the Nterminus (aa 20-25). This result supports the reviewer’s comment regarding the low level of expression of endogenous p53 that is insufficient for detection in our experiments.
In summary, in line with the reviewer’s comment that ‘under normal physiological conditions p53 expression is usually low,’ we could not detect p53 with an anti-DO-1 antibody. Thus, we proceeded with V5/FLAG-tagged p53 for detection of the effects of the isoforms on p53 stability and function. We also found that protein expression in H1299 cells was more easily detectable than in A549 cells (Compare Author response image 1A and B). Thus, we decided to continue with the H1299 cells (p53-null), which would serve as a more suitable model system for this study.
(2) We agree with the reviewer that ‘It is hard to differentiate if aggregation of full-length p53 happens only in overexpression scenario’. However, it is not impossible to imagine that such aggregation of FLp53 happens under conditions when p53 and its isoforms are over-expressed in the cell. Although the exact physiological context is not known and beyond the scope of the current work, our results indicate that at higher expression, p53 isoforms drive aggregation of FLp53. Given the challenges of detecting endogenous FLp53, we had to rely on the results obtained with plasmid mediated expression of p53 and its isoforms in p53-null cells.
Author response image 1.
Comparative analysis of protein expression in A549 and H1299 cells. (A) A549 cells (p53 wild-type) were treated with etoposide to induce endogenous wild-type p53 expression. To assess the effects of FLp53 and its isoforms Δ133p53 and Δ160p53 on endogenous wild-type p53 aggregation, A549 cells were transfected with 2 μg of V5-tagged p53 expression plasmids, with or without etoposide (20μM for 8h) treatment. Western blot analysis was done with the anti-V5 (rabbit) to detect V5-tagged proteins and anti-DO-1 (mouse), the latter detects both endogenous wild-type p53 and V5-tagged FLp53. The merged image corresponds to the overlay between the V5 and DO1 antibody signals. (B) H1299 cells (p53-null) were transfected with 2 μg V5tagged p53 expression plasmids or the empty vector control pcDNA3.1. Western blot analysis was done with the anti-V5 (mouse) antibody.
(2) Can presence of mutant P53 isoforms can cause functional impairment of wild type full length endogenous P53? That could be tested as well using similar ChIP assay authors has performed, but instead of antibody against the Tagged protein if the authors could check endogenous P53 enrichment in the gene promoter such as P21 following overexpression of mutant isoforms. May be introducing a condition such as DNA damage in such experiment might help where endogenous P53 is induced and more prone to bind to P53 target such as P21.
Thank you very much for your valuable comments and suggestions. To investigate the potential functional impairment of endogenous wild-type p53 by p53 isoforms, we initially utilized A549 cells (p53 wild-type), aiming to monitor endogenous wild-type p53 expression following DNA damage. However, as mentioned and demonstrated in Author response image 1, endogenous p53 expression was too low to be detected under these conditions, making the ChIP assay for analyzing endogenous p53 activity unfeasible. Thus, we decided to utilize plasmid-based expression of FLp53 and focus on the potential functional impairment induced by the isoforms.
(3) On similar lines, authors described:
"To test this hypothesis, we escalated the ratio of FLp53 to isoforms to 1:10. As expected, the activity of all four promoters decreased significantly at this ratio (Figure 4A-D). Notably, Δ160p53 showed a more potent inhibitory effect than Δ133p53 at the 1:5 ratio on all promoters except for the p21 promoter, where their impacts were similar (Figure 4E-H). However, at the 1:10 ratio, Δ133p53 and Δ160p53 had similar effects on all transactivation except for the MDM2 promoter (Figure 4E-H)."
Again, in such assay authors used ratio 1:5 to 1:10 full length vs mutant. How authors justify this result in context (which is more relevant context) where one allele is Wild type (functional P53) and another allele is mutated (truncated, can induce aggregation). In this case one would except 1:1 ratio of full-length vs mutant protein, unless other regulation is going which induces expression of mutant isoforms more than wild type full length protein. Probably discussing on these lines might provide more physiological relevance to the observed data.
Thank you for raising this point regarding the physiological relevance of the ratios used in our study.
(1) In the revised manuscript (lines 193-195), we added in this direction that “The elevated Δ133p53 protein modulates p53 target genes such as miR‑34a and p21, facilitating cancer development(2, 3). To mimic conditions where isoforms are upregulated relative to FLp53, we increased the ratios to 1:5 and 1:10.” This approach aims to simulate scenarios where isoforms accumulate at higher levels than FLp53, which may be relevant in specific contexts, as also elaborated above.
(2) Regarding the issue of protein expression, where one allele is wild-type and the other is isoform, this assumption is not valid in most contexts. First, human cells have two copies of TPp53 gene (one from each parent). Second, the TP53 gene has two distinct promoters: the proximal promoter (P1) primarily regulates FLp53 and ∆40p53, whereas the second promoter (P2) regulates ∆133p53 and ∆160p53(4, 5). Additionally, ∆133TP53 is a p53 target gene(6, 7) and the expression of Δ133p53 and FLp53 is dynamic in response to various stimuli. Third, the expression of p53 isoforms is regulated at multiple levels, including transcriptional, post-transcriptional, translational, and post-translational processing(8). Moreover, different degradation mechanisms modify the protein level of p53 isoforms and FLp53(8). These differential regulation mechanisms are regulated by various stimuli, and therefore, the 1:1 ratio of FLp53 to ∆133p53 or ∆160p53 may be valid only under certain physiological conditions. In line with this, varied expression levels of FLp53 and its isoforms, including ∆133p53 and ∆160p53, have been reported in several studies(3, 4, 9, 10).
(3) In our study, using the pcDNA 3.1 vector under the human cytomegalovirus (CMV) promoter, we observed moderately higher expression levels of ∆133p53 and ∆160p53 relative to FLp53 (Author response image 1B). This overexpression scenario provides a model for studying conditions where isoform accumulation might surpass physiological levels, impacting FLp53 function. By employing elevated ratios of these isoforms to FLp53, we aim to investigate the potential effects of isoform accumulation on FLp53.
(4) Finally does this altered function of full length P53 (preferably endogenous one) in presence of truncated P53 has any phenotypic consequence on the cells (if authors choose a cell type which is having wild type functional P53). Doing assay such as apoptosis/cell cycle could help us to get this visualization.
Thank you for your insightful comments. In the experiment with A549 cells (p53 wild-type), endogenous p53 levels were too low to be detected, even after DNA damage induction. The evaluation of the function of endogenous p53 in the presence of isoforms is hindered, as mentioned above. In the revised manuscript, we utilized H1299 cells with overexpressed proteins for apoptosis studies using the Caspase-Glo® 3/7 assay (Figure 7). This has been shown in the Results section (lines 254-269). “The Δ133p53 and Δ160p53 proteins block pro-apoptotic function of FLp53.
One of the physiological read-outs of FLp53 is its ability to induce apoptotic cell death(11). To investigate the effects of p53 isoforms Δ133p53 and Δ160p53 on FLp53-induced apoptosis, we measured caspase-3 and -7 activities in H1299 cells expressing different p53 isoforms (Figure 7). Caspase activation is a key biochemical event in apoptosis, with the activation of effector caspases (caspase-3 and -7) ultimately leading to apoptosis(12). The caspase-3 and -7 activities induced by FLp53 expression was approximately 2.5 times higher than that of the control vector (Figure 7). Co-expression of FLp53 and the isoforms Δ133p53 or Δ160p53 at a ratio of 1: 5 significantly diminished the apoptotic activity of FLp53 (Figure 7). This result aligns well with our reporter gene assay, which demonstrated that elevated expression of Δ133p53 and Δ160p53 impaired the expression of apoptosis-inducing genes BAX and PUMA (Figure 4G and H). Moreover, a reduction in the apoptotic activity of FLp53 was observed irrespective of whether Δ133p53 or Δ160p53 protein was expressed with or without a FLAG tag (Figure 7). This result, therefore, also suggests that the FLAG tag does not affect the apoptotic activity or other physiological functions of FLp53 and its isoforms. Overall, the overexpression of p53 isoforms Δ133p53 and Δ160p53 significantly attenuates FLp53-induced apoptosis, independent of the protein tagging with the FLAG antibody epitope.”
Referees cross-commenting
I think the comments from the other reviewers are very much reasonable and logical.
Especially all 3 reviewers have indicated, a better way to visualize the aggregation of full-length wild type P53 by truncated P53 (such as looking at endogenous P53# by reviewer 1, having fluorescent tag #by reviewer 2 and reviewer 3 raised concern on the FLAG tag) would add more value to the observation.
Thank you for these comments. The endogenous p53 protein was undetectable in A549 cells induced by etoposide (Figure R1A). Therefore, we conducted experiments using FLAG/V5-tagged FLp53. To avoid any potential side effects of the FLAG tag on p53 aggregation, we introduced untagged p53 isoforms in the H1299 cells and performed subcellular fractionation. Our revised results, consistent with previous FLAG-tagged p53 isoforms findings, demonstrate that co-expression of untagged isoforms with FLAG-tagged FLp53 significantly induced the aggregation of FLAG-FLp53, while no aggregation was observed when FLAG-tagged FLp53 was expressed alone (Supplementary Figure 6). These results clearly indicate that the FLAG tag itself does not contribute to protein aggregation.
Additionally, we utilized the A11 antibody to detect protein aggregation, providing additional validation (Figure 8 from Jean-Christophe Bourdon et al. Genes Dev. 2005;19:2122-2137). Given that the fluorescent proteins (~30 kDa) are substantially bigger than the tags used here (~1 kDa) and may influence oligomerization (especially GFP), stability, localization, and function of p53 and its isoforms, we avoided conducting these vital experiments with such artificial large fusions.
Reviewer #1 (Significance):
The work in significant, since it points out more mechanistic insight how wild type full length P53 could be inactivated in the presence of truncated isoforms, this might offer new opportunity to recover P53 function as treatment strategies against cancer.
Thank you for your insightful comments. We appreciate your recognition of the significance of our work in providing mechanistic insights into how wild-type FLp53 can be inactivated by truncated isoforms. We agree that these findings have potential for exploring new strategies to restore p53 function as a therapeutic approach against cancer.
Reviewer #2 (Evidence, reproducibility and clarity):
The manuscript by Zhao and colleagues presents a novel and compelling study on the p53 isoforms, Δ133p53 and Δ160p53, which are associated with aggressive cancer types. The main objective of the study was to understand how these isoforms exert a dominant negative effect on full-length p53 (FLp53). The authors discovered that the Δ133p53 and Δ160p53 proteins exhibit impaired binding to p53-regulated promoters. The data suggest that the predominant mechanism driving the dominant-negative effect is the coaggregation of FLp53 with Δ133p53 and Δ160p53.
This study is innovative, well-executed, and supported by thorough data analysis. However, the authors should address the following points:
(1) Introduction on Aggregation and Co-aggregation: Given that the focus of the study is on the aggregation and co-aggregation of the isoforms, the introduction should include a dedicated paragraph discussing this issue. There are several original research articles and reviews that could be cited to provide context.
Thank you very much for the valuable comments. We have added the following paragraph in the revised manuscript (lines 74-82): “Protein aggregation has become a central focus of modern biology research and has documented implications in various diseases, including cancer(13, 14, 15). Protein aggregates can be of different types ranging from amorphous aggregates to highly structured amyloid or fibrillar aggregates, each with different physiological implications. In the case of p53, whether protein aggregation, and in particular, co-aggregation with large N-terminal deletion isoforms, plays a mechanistic role in its inactivation is yet underexplored. Interestingly, the Δ133p53β isoform has been shown to aggregate in several human cancer cell lines(16). Additionally, the Δ40p53α isoform exhibits a high aggregation tendency in endometrial cancer cells(17). Although no direct evidence exists for Δ160p53 yet, these findings imply that p53 isoform aggregation may play a major role in their mechanisms of actions.”
(2) Antibody Use for Aggregation: To strengthen the evidence for aggregation, the authors should consider using antibodies that specifically bind to aggregates.
Thank you for your insightful suggestion. We addressed protein aggregation using the A11 antibody which specifically recognizes amyloid-like protein aggregates. We analyzed insoluble nuclear pellet samples prepared under identical conditions as described in Figure 6B. To confirm the presence of p53 proteins, we employed the anti-p53 M19 antibody (Santa Cruz, Cat No. sc-1312) to detect bands corresponding to FLp53 and its isoforms Δ133p53 and Δ160p53. The monomer FLp53 was not detected (Figure 8, lower panel, Jean-Christophe Bourdon et al. Genes Dev. 2005;19:2122-2137), which may be attributed to the lower binding affinity of the anti-p53 M19 antibody to it. These samples were also immunoprecipitated using the A11 antibody (Thermo Fischer Scientific, Cat No. AHB0052) to detect aggregated proteins. Interestingly, FLp53 and its isoforms, Δ133p53 and Δ160p53, were clearly visible with Anti-A11 antibody when co-expressed at a 1:5 ratio suggesting that they underwent co-aggregation. However, no FLp53 aggregates were observed when it was expressed alone (Author response image 2). These results support the conclusion in our manuscript that Δ133p53 and Δ160p53 drive FLp53 aggregation.
Author response image 2.
Induction of FLp53 Aggregation by p53 Isoforms Δ133p53 and Δ160p53. H1299 cells transfected with the FLAG-tagged FLp53 and V5-tagged Δ133p53 or Δ160p53 at a 1:5 ratio. The cells were subjected to subcellular fractionation, and the resulting insoluble nuclear pellet was resuspended in RIPA buffer. The samples were heated at 95°C until the pellet was completely dissolved, and then analyzed by Western blotting. Immunoprecipitation was performed using the A11 antibody, which specifically recognizes amyloid protein aggregates, and the anti-p53 M19 antibody, which detects FLp53 as well as its isoforms Δ133p53 and Δ160p53.
(3) Fluorescence Microscopy: Live-cell fluorescence microscopy could be employed to enhance visualization by labeling FLp53 and the isoforms with different fluorescent markers (e.g., EGFP and mCherry tags).
We appreciate the suggestion to use live-cell fluorescence microscopy with EGFP and mCherry tags for the visualization FLp53 and its isoforms. While we understand the advantages of live-cell imaging with EGFP / mCherry tags, we restrained us from doing such fusions as the GFP or corresponding protein tags are very big (~30 kDa) with respect to the p53 isoform variants (~30 kDa). Other studies have shown that EGFP and mCherry fusions can alter protein oligomerization, solubility and aggregation(18, 19) Moreover, most fluorescence proteins are prone to dimerization (i.e. EGFP) or form obligate tetramers (DsRed)(20, 21, 22), potentially interfering with the oligomerization and aggregation properties of p53 isoforms, particularly Δ133p53 and Δ160p53.
Instead, we utilized FLAG- or V5-tag-based immunofluorescence microscopy, a well-established and widely accepted method for visualizing p53 proteins. This method provided precise localization and reliable quantitative data, which we believe meet the needs of the current study. We believe our chosen method is both appropriate and sufficient for addressing the research question.
Reviewer #2 (Significance):
The manuscript by Zhao and colleagues presents a novel and compelling study on the p53 isoforms, Δ133p53 and Δ160p53, which are associated with aggressive cancer types. The main objective of the study was to understand how these isoforms exert a dominant negative effect on full-length p53 (FLp53). The authors discovered that the Δ133p53 and Δ160p53 proteins exhibit impaired binding to p53-regulated promoters. The data suggest that the predominant mechanism driving the dominant-negative effect is the coaggregation of FLp53 with Δ133p53 and Δ160p53.
We sincerely thank the reviewer for the thoughtful and positive comments on our manuscript and for highlighting the significance of our findings on the p53 isoforms, Δ133p53 and Δ160p53.
Reviewer #3 (Evidence, reproducibility and clarity):
In this manuscript entitled "Δ133p53 and Δ160p53 isoforms of the tumor suppressor protein p53 exert dominant-negative effect primarily by coaggregation", the authors suggest that the Δ133p53 and Δ160p53 isoforms have high aggregation propensity and that by co-aggregating with canonical p53 (FLp53), they sequestrate it away from DNA thus exerting a dominantnegative effect over it.
First, the authors should make it clear throughout the manuscript, including the title, that they are investigating Δ133p53α and Δ160p53α since there are 3 Δ133p53 isoforms (α, β, γ), and 3 Δ160p53 isoforms (α, β, γ).
Thank you for your suggestion. We understand the importance of clearly specifying the isoforms under study. Following your suggestion, we have added α in the title, abstract, and introduction and added the following statement in the Introduction (lines 57-59): “For convenience and simplicity, we have written Δ133p53 and Δ160p53 to represent the α isoforms (Δ133p53α and Δ160p53α) throughout this manuscript.”
One concern is that the authors only consider and explore Δ133p53α and Δ160p53α isoforms as exclusively oncogenic and FLp53 dominant-negative while not discussing evidences of different activities. Indeed, other manuscripts have also shown that Δ133p53α is non-oncogenic and non-mutagenic, do not antagonize every single FLp53 functions and are sometimes associated with good prognosis. To cite a few examples:
(1) Hofstetter G. et al. D133p53 is an independent prognostic marker in p53 mutant advanced serous ovarian cancer. Br. J. Cancer 2011, 105, 15931599.
(2) Bischof, K. et al. Influence of p53 Isoform Expression on Survival in HighGrade Serous Ovarian Cancers. Sci. Rep. 2019, 9,5244.
(3) Knezovi´c F. et al. The role of p53 isoforms' expression and p53 mutation status in renal cell cancer prognosis. Urol. Oncol. 2019, 37, 578.e1578.e10.
(4) Gong, L. et al. p53 isoform D113p53/D133p53 promotes DNA doublestrand break repair to protect cell from death and senescence in response to DNA damage. Cell Res. 2015, 25, 351-369.
(5) Gong, L. et al. p53 isoform D133p53 promotes efficiency of induced pluripotent stem cells and ensures genomic integrity during reprogramming. Sci. Rep. 2016, 6, 37281.
(6) Horikawa, I. et al. D133p53 represses p53-inducible senescence genes and enhances the generation of human induced pluripotent stem cells. Cell Death Differ. 2017, 24, 1017-1028.
(7) Gong, L. p53 coordinates with D133p53 isoform to promote cell survival under low-level oxidative stress. J. Mol. Cell Biol. 2016, 8, 88-90.
Thank you very much for your comment and for highlighting these important studies.
We agree that Δ133p53 isoforms exhibit complex biological functions, with both oncogenic and non-oncogenic potentials. However, our mission here was primarily to reveal the molecular mechanism for the dominant-negative effects exerted by the Δ133p53α and Δ160p53α isoforms on FLp53 for which the Δ133p53α and Δ160p53α isoforms are suitable model systems. Exploring the oncogenic potential of the isoforms is beyond the scope of the current study and we have not claimed anywhere that we are reporting that. We have carefully revised the manuscript and replaced the respective terms e.g. ‘prooncogenic activity’ with ‘dominant-negative effect’ in relevant places (e.g. line 90). We have now also added a paragraph with suitable references that introduces the oncogenic and non-oncogenic roles of the p53 isoforms.
After reviewing the papers you cited, we are not sure that they reflect on oncogenic /non-oncogenic role of the Δ133p53α isoform in different cancer cases. Although our study is not about the oncogenic potential of the isoforms, we have summarized the key findings below:
(1) Hofstetter et al., 2011: Demonstrated that Δ133p53α expression improved recurrence-free and overall survival (in a p53 mutant induced advanced serous ovarian cancer, suggesting a potential protective role in this context.
(2) Bischof et al., 2019: Found that Δ133p53 mRNA can improve overall survival in high-grade serous ovarian cancers. However, out of 31 patients, only 5 belong to the TP53 wild-type group, while the others carry TP53 mutations.
(3) Knezović et al., 2019: Reported downregulation of Δ133p53 in renal cell carcinoma tissues with wild-type p53 compared to normal adjacent tissue, indicating a potential non-oncogenic role, but not conclusively demonstrating it.
(4) Gong et al., 2015: Showed that Δ133p53 antagonizes p53-mediated apoptosis and promotes DNA double-strand break repair by upregulating RAD51, LIG4, and RAD52 independently of FLp53.
(5) Gong et al., 2016: Demonstrated that overexpression of Δ133p53 promotes efficiency of cell reprogramming by its anti-apoptotic function and promoting DNA DSB repair. The authors hypotheses that this mechanism is involved in increasing RAD51 foci formation and decrease γH2AX foci formation and chromosome aberrations in induced pluripotent stem (iPS) cells, independent of FL p53.
(6) Horikawa et al., 2017: Indicated that induced pluripotent stem cells derived from fibroblasts that overexpress Δ133p53 formed noncancerous tumors in mice compared to induced pluripotent stem cells derived from fibroblasts with complete p53 inhibition. Thus, Δ133p53 overexpression is "non- or less oncogenic and mutagenic" compared to complete p53 inhibition, but it still compromises certain p53-mediated tumor-suppressing pathways. “Overexpressed Δ133p53 prevented FL-p53 from binding to the regulatory regions of p21WAF1 and miR-34a promoters, providing a mechanistic basis for its dominant-negative
inhibition of a subset of p53 target genes.”
(7) Gong, 2016: Suggested that Δ133p53 promotes cell survival under lowlevel oxidative stress, but its role under different stress conditions remains uncertain.
We have revised the Introduction to provide a more balanced discussion of Δ133p53’s dule role (lines 62-73):
“The Δ133p53 isoform exhibit complex biological functions, with both oncogenic and non-oncogenic potentials. Recent studies demonstrate the non-oncogenic yet context-dependent role of the Δ133p53 isoform in cancer development. Δ133p53 expression has been reported to correlate with improved survival in patients with TP53 mutations(23, 24), where it promotes cell survival in a nononcogenic manner(25, 26), especially under low oxidative stress(27). Alternatively, other recent evidences emphasize the notable oncogenic functions of Δ133p53 as it can inhibit p53-dependent apoptosis by directly interacting with the FLp53 (4, 6). The oncogenic function of the newly identified Δ160p53 isoform is less known, although it is associated with p53 mutation-driven tumorigenesis(28) and in melanoma cells’ aggressiveness(10). Whether or not the Δ160p53 isoform also impedes FLp53 function in a similar way as Δ133p53 is an open question. However, these p53 isoforms can certainly compromise p53-mediated tumor suppression by interfering with FLp53 binding to target genes such as p21 and miR-34a(2, 29) by dominant-negative effect, the exact mechanism is not known.” On the figures presented in this manuscript, I have three major concerns:
(1) Most results in the manuscript rely on the overexpression of the FLAGtagged or V5-tagged isoforms. The validation of these construct entirely depends on Supplementary figure 3 which the authors claim "rules out the possibility that the FLAG epitope might contribute to this aggregation. However, I am not entirely convinced by that conclusion. Indeed, the ratio between the "regular" isoform and the aggregates is much higher in the FLAG-tagged constructs than in the V5-tagged constructs. We can visualize the aggregates easily in the FLAG-tagged experiment, but the imaging clearly had to be overexposed (given the white coloring demonstrating saturation of the main bands) to visualize them in the V5-tagged experiments. Therefore, I am not convinced that an effect of the FLAG-tag can be ruled out and more convincing data should be added.
Thank you for raising this important concern. We have carefully considered your comments and have made several revisions to clarify and strengthen our conclusions.
First, to address the potential influence of the FLAG and V5 tags on p53 isoform aggregation, we have revised Figure 2 and removed the previous Supplementary Figure 3, where non-specific antibody bindings and higher molecular weight aggregates were not clearly interpretable. In the revised Figure 2, we have removed these potential aggregates, improving the clarity and accuracy of the data.
To further rule out any tag-related artifacts, we conducted a coimmunoprecipitation assay with FLAG-tagged FLp53 and untagged Δ133p53 and Δ160p53 isoforms. The results (now shown in the new Supplementary Figure 3) completely agree with our previous result with FLAG-tagged and V5tagged Δ133p53 and Δ160p53 isoforms and show interaction between the partners. This indicates that the FLAG / V5-tags do not influence / interfere with the interaction between FLp53 and the isoforms. We have still used FLAGtagged FLp53 as the endogenous p53 was undetectable and the FLAG-tagged FLp53 did not aggregate alone.
In the revised paper, we added the following sentences (Lines 146-152): “To rule out the possibility that the observed interactions between FLp53 and its isoforms Δ133p53 and Δ160p53 were artifacts caused by the FLAG and V5 antibody epitope tags, we co-expressed FLAG-tagged FLp53 with untagged Δ133p53 and Δ160p53. Immunoprecipitation assays demonstrated that FLAGtagged FLp53 could indeed interact with the untagged Δ133p53 and Δ160p53 isoforms (Supplementary Figure 3, lanes 3 and 4), confirming formation of hetero-oligomers between FLp53 and its isoforms. These findings demonstrate that Δ133p53 and Δ160p53 can oligomerize with FLp53 and with each other.”
Additionally, we performed subcellular fractionation experiments to compare the aggregation and localization of FLAG-tagged FLp53 when co-expressed either with V5-tagged or untagged Δ133p53/Δ160p53. In these experiments, the untagged isoforms also induced FLp53 aggregation, mirroring our previous results with the tagged isoforms (Supplementary Figure 5). We’ve added this result in the revised manuscript (lines 236-245): “To exclude the possibility that FLAG or V5 tags contribute to protein aggregation, we also conducted subcellular fractionation of H1299 cells expressing FLAG-tagged FLp53 along with untagged Δ133p53 or Δ160p53 at a 1:5 ratio. The results showed (Supplementary Figure 6) a similar distribution of FLp53 across cytoplasmic, nuclear, and insoluble nuclear fractions as in the case of tagged Δ133p53 or Δ160p53 (Figure 6A to D). Notably, the aggregation of untagged Δ133p53 or Δ160p53 markedly promoted the aggregation of FLAG-tagged FLp53 (Supplementary Figure 6B and D), demonstrating that the antibody epitope tags themselves do not contribute to protein aggregation.”
We’ve also discussed this in the Discussion section (lines 349-356): “In our study, we primarily utilized an overexpression strategy involving FLAG/V5tagged proteins to investigate the effects of p53 isoforms Δ133p53 and Δ160p53 on the function of FLp53. To address concerns regarding potential overexpression artifacts, we performed the co-immunoprecipitation (Supplementary Figure 6) and caspase-3 and -7 activity (Figure 7) experiments with untagged Δ133p53 and Δ160p53. In both experimental systems, the untagged proteins behaved very similarly to the FLAG/V5 antibody epitopecontaining proteins (Figures 6 and 7 and Supplementary Figure 6). Hence, the C-terminal tagging of FLp53 or its isoforms does not alter the biochemical and physiological functions of these proteins.”
In summary, the revised data set and newly added experiments provide strong evidence that neither the FLAG nor the V5 tag contributes to the observed p53 isoform aggregation.
(2) The authors demonstrate that to visualize the dominant-negative effect, Δ133p53α and Δ160p53α must be "present in a higher proportion than FLp53 in the tetramer" and the need at least a transfection ratio 1:5 since the 1:1 ration shows no effect. However, in almost every single cell type, FLp53 is far more expressed than the isoforms which make it very unlikely to reach such stoichiometry in physiological conditions and make me wonder if this mechanism naturally occurs at endogenous level. This limitation should be at least discussed.
Thank you for your insightful comment. However, evidence suggests that the expression levels of these isoforms such as Δ133p53, can be significantly elevated relative to FLp53 in certain physiological conditions(3, 4, 9). For example, in some breast tumors, with Δ133p53 mRNA is expressed at a much levels than FLp53, suggesting a distinct expression profile of p53 isoforms compared to normal breast tissue(4). Similarly, in non-small cell lung cancer and the A549 lung cancer cell line, the expression level of Δ133p53 transcript is significantly elevated compared to non-cancerous cells(3). Moreover, in specific cholangiocarcinoma cell lines, the Δ133p53 /TAp53 expression ratio has been reported to increase to as high as 3:1(9). These observations indicate that the dominant-negative effect of isoform Δ133p53 on FLp53 can occur under certain pathological conditions where the relative amounts of the FLp53 and the isoforms would largely vary. Since data on the Δ160p53 isoform are scarce, we infer that the long N-terminal truncated isoforms may share a similar mechanism.
(3) Figure 5C: I am concerned by the subcellular location of the Δ133p53α and Δ160p53α as they are commonly considered nuclear and not cytoplasmic as shown here, particularly since they retain the 3 nuclear localization sequences like the FLp53 (Bourdon JC et al. 2005; Mondal A et al. 2018; Horikawa I et al, 2017; Joruiz S. et al, 2024). However, Δ133p53α can form cytoplasmic speckles (Horikawa I et al, 2017) when it colocalizes with autophagy markers for its degradation.
The authors should discuss this issue. Could this discrepancy be due to the high overexpression level of these isoforms? A co-staining with autophagy markers (p62, LC3B) would rule out (or confirm) activation of autophagy due to the overwhelming expression of the isoform.
Thank you for your thoughtful comments. We have thoroughly reviewed all the papers you recommended (Bourdon JC et al., 2005; Mondal A et al., 2018; Horikawa I et al., 2017; Joruiz S. et al., 2024)(4, 29, 30, 31). Among these, only the study by Bourdon JC et al. (2005) provided data regarding the localization of Δ133p53(4). Interestingly, their findings align with our observations, indicating that the protein does not exhibit predominantly nuclear localization in the Figure 8 from Jean-Christophe Bourdon et al. Genes Dev. 2005;19:2122-2137. The discrepancy may be caused by a potentially confusing statement in that paper(4).
The localization of p53 is governed by multiple factors, including its nuclear import and export(32). The isoforms Δ133p53 and Δ160p53 contain three nuclear localization sequences (NLS)(4). However, the isoforms Δ133p53 and Δ160p53 were potentially trapped in the cytoplasm by aggregation and masking the NLS. This mechanism would prevent nuclear import.
Further, we acknowledge that Δ133p53 co-aggregates with autophagy substrate p62/SQSTM1 and autophagosome component LC3B in cytoplasm by autophagic degradation during replicative senescence(33). We agree that high overexpression of these aggregation-prone proteins may induce endoplasmic reticulum (ER) stress and activates autophagy(34). This could explain the cytoplasmic localization in our experiments. However, it is also critical to consider that we observed aggregates in both the cytoplasm and the nucleus (Figures 6B and E and Supplementary Figure 6B). While cytoplasmic localization may involve autophagy-related mechanisms, the nuclear aggregates likely arise from intrinsic isoform properties, such as altered protein folding, independent of autophagy. These dual localizations reflect the complex behavior of Δ133p53 and Δ160p53 isoforms under our experimental conditions.
In the revised manuscript, we discussed this in Discussion (lines 328-335): “Moreover, the observed cytoplasmic isoform aggregates may reflect autophagy-related degradation, as suggested by the co-localization of Δ133p53 with autophagy substrate p62/SQSTM1 and autophagosome component LC3B(33). High overexpression of these aggregation-prone proteins could induce endoplasmic reticulum stress and activate autophagy(34). Interestingly, we also observed nuclear aggregation of these isoforms (Figure 6B and E and Supplementary Figure 6B), suggesting that distinct mechanisms, such as intrinsic properties of the isoforms, may govern their localization and behavior within the nucleus. This dual localization underscores the complexity of Δ133p53 and Δ160p53 behavior in cellular systems.”
Minor concerns:
- Figure 1A: the initiation of the "Δ140p53" is shown instead of "Δ40p53"
Thank you! The revised Figure 1A has been created in the revised paper.
- Figure 2A: I would like to see the images cropped a bit higher, so the cut does not happen just above the aggregate bands
Thank you for this suggestion. We’ve changed the image and the new Figure 2 has been shown in the revised paper.
- Figure 3C: what ratio of FLp53/Delta isoform was used?
We have added the ratio in the figure legend of Figure 3C (lines 845-846) “Relative DNA-binding of the FLp53-FLAG protein to the p53-target gene promoters in the presence of the V5-tagged protein Δ133p53 or Δ160p53 at a 1: 1 ratio.”
- Figure 3C suggests that the "dominant-negative" effect is mostly senescencespecific as it does not affect apoptosis target genes, which is consistent with Horikawa et al, 2017 and Gong et al, 2016 cited above. Furthermore, since these two references and the others from Gong et al. show that Δ133p53α increases DNA repair genes, it would be interesting to look at RAD51, RAD52 or Lig4, and maybe also induce stress.
Thank you for your thoughtful comments and suggestions. In Figure 3C, the presence of Δ133p53 or Δ160p53 only significantly reduced the binding of FLp53 to the p21 promoter. However, isoforms Δ133p53 and Δ160p53 demonstrated a significant loss of DNA-binding activity at all four promoters: p21, MDM2, and apoptosis target genes BAX and PUMA (Figure 3B). This result suggests that Δ133p53 and Δ160p53 have the potential to influence FLp53 function due to their ability to form hetero-oligomers with FLp53 or their intrinsic tendency to aggregate. To further investigate this, we increased the isoform to FLp53 ratio in Figure 4, which demonstrate that the isoforms Δ133p53 and Δ160p53 exert dominant-negative effects on the function of FLp53.
These results demonstrate that the isoforms can compromise p53-mediated pathways, consistent with Horikawa et al. (2017), which showed that Δ133p53α overexpression is "non- or less oncogenic and mutagenic" compared to complete p53 inhibition, but still affects specific tumor-suppressing pathways. Furthermore, as noted by Gong et al. (2016), Δ133p53’s anti-apoptotic function under certain conditions is independent of FLp53 and unrelated to its dominantnegative effects.
We appreciate your suggestion to investigate DNA repair genes such as RAD51, RAD52, or Lig4, especially under stress conditions. While these targets are intriguing and relevant, we believe that our current investigation of p53 targets in this manuscript sufficiently supports our conclusions regarding the dominant-negative effect. Further exploration of additional p53 target genes, including those involved in DNA repair, will be an important focus of our future studies.
- Figure 5A and B: directly comparing the level of FLp53 expressed in cytoplasm or nucleus to the level of Δ133p53α and Δ160p53α expressed in cytoplasm or nucleus does not mean much since these are overexpressed proteins and therefore depend on the level of expression. The authors should rather compare the ratio of cytoplasmic/nuclear FLp53 to the ratio of cytoplasmic/nuclear Δ133p53α and Δ160p53α.
Thank you very much for this valuable suggestion. In the revised paper, Figure 5B has been recreated. Changes have been made in lines 214215: “The cytoplasm-to-nucleus ratio of Δ133p53 and Δ160p53 was approximately 1.5-fold higher than that of FLp53 (Figure 5B).”
Referees cross-commenting
I agree that the system needs to be improved to be more physiological.
Just to precise, the D133 and D160 isoforms are not truncated mutants, they are naturally occurring isoforms expressed in almost every normal human cell type from an internal promoter within the TP53 gene.
Using overexpression always raises concerns, but in this case, I am even more careful because the isoforms are almost always less expressed than the FLp53, and here they have to push it 5 to 10 times more expressed than the FLp53 to see the effect which make me fear an artifact effect due to the overwhelming overexpression (which even seems to change the normal localization of the protein).
To visualize the endogenous proteins, they will have to change cell line as the H1299 they used are p53 null.
Thank you for these comments. We’ve addressed the motivation of overexpression in the above responses. We needed to use the plasmid constructs in the p53-null cells to detect the proteins but the expression level was certainly not ‘overwhelmingly high’.
First, we tried the A549 cells (p53 wild-type) under DNA damage conditions, but the endogenous p53 protein was undetectable. Second, several studies reported increased Δ133p53 level compared to wild-type p53 and that it has implications in tumor development(2, 3, 4, 9). Third, the apoptosis activity of H1299 cells overexpressing p53 proteins was analyzed in the revised manuscript (Figure 7). The apoptotic activity induced by FLp53 expression was approximately 2.5 times higher than that of the control vector under identical plasmid DNA transfection conditions (Figure 7). These results rule out the possibility that the plasmid-based expression of p53 and its isoforms introduced artifacts in the results. We’ve discussed this in the Results section (lines 254269).
Reviewer #3 (Significance):
Overall, the paper is interesting particularly considering the range of techniques used which is the main strength.
The main limitation to me is the lack of contradictory discussion as all argumentation presents Δ133p53α and Δ160p53α exclusively as oncogenic and strictly FLp53 dominant-negative when, particularly for Δ133p53α, a quite extensive literature suggests a not so clear-cut activity.
The aggregation mechanism is reported for the first time for Δ133p53α and Δ160p53α, although it was already published for Δ40p53α, Δ133p53β or in mutant p53.
This manuscript would be a good basic research addition to the p53 field to provide insight in the mechanism for some activities of some p53 isoforms.
My field of expertise is the p53 isoforms which I have been working on for 11 years in cancer and neuro-degenerative diseases
Thank you very much for your positive and critical comments. We’ve included a fair discussion on the oncogenic and non-oncogenic function of Δ133p53 in the Introduction following your suggestion (lines 62-73).
References
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(9) Nutthasirikul N, Limpaiboon T, Leelayuwat C, Patrakitkomjorn S, Jearanaikoon P. Ratio disruption of the ∆133p53 and TAp53 isoform equilibrium correlates with poor clinical outcome in intrahepatic cholangiocarcinoma. International journal of oncology 42, 1181-1188 (2013).
(10) Tadijan A, et al. Altered Expression of Shorter p53 Family Isoforms Can Impact Melanoma Aggressiveness. Cancers 13, (2021).
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(16) Arsic N, et al. Δ133p53β isoform pro-invasive activity is regulated through an aggregation-dependent mechanism in cancer cells. Nature communications 12, 5463 (2021).
(17) Melo Dos Santos N, et al. Loss of the p53 transactivation domain results in high amyloid aggregation of the Δ40p53 isoform in endometrial carcinoma cells. The Journal of biological chemistry 294, 9430-9439 (2019).
(18) Mestrom L, et al. Artificial Fusion of mCherry Enhances Trehalose Transferase Solubility and Stability. Applied and environmental microbiology 85, (2019).
(19) Kaba SA, Nene V, Musoke AJ, Vlak JM, van Oers MM. Fusion to green fluorescent protein improves expression levels of Theileria parva sporozoite surface antigen p67 in insect cells. Parasitology 125, 497-505 (2002).
(20) Snapp EL, et al. Formation of stacked ER cisternae by low affinity protein interactions. The Journal of cell biology 163, 257-269 (2003).
(21) Jain RK, Joyce PB, Molinete M, Halban PA, Gorr SU. Oligomerization of green fluorescent protein in the secretory pathway of endocrine cells. The Biochemical journal 360, 645-649 (2001).
(22) Campbell RE, et al. A monomeric red fluorescent protein. Proceedings of the National Academy of Sciences of the United States of America 99, 7877-7882 (2002).
(23) Hofstetter G, et al. Δ133p53 is an independent prognostic marker in p53 mutant advanced serous ovarian cancer. British journal of cancer 105, 1593-1599 (2011).
(24) Bischof K, et al. Influence of p53 Isoform Expression on Survival in High-Grade Serous Ovarian Cancers. Scientific reports 9, 5244 (2019).
(25) Gong L, et al. p53 isoform Δ113p53/Δ133p53 promotes DNA double-strand break repair to protect cell from death and senescence in response to DNA damage. Cell research 25, 351-369 (2015).
(26) Gong L, et al. p53 isoform Δ133p53 promotes efficiency of induced pluripotent stem cells and ensures genomic integrity during reprogramming. Scientific reports 6, 37281 (2016).
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(33) Horikawa I, et al. Autophagic degradation of the inhibitory p53 isoform Δ133p53α as a regulatory mechanism for p53-mediated senescence. Nature communications 5, 4706 (2014).
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journals.plos.org journals.plos.org
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We established GapR-GFP, a prokaryotic DNA-binding protein that recognizes transcriptionally-induced overtwisted DNA, as a live visual fluorescent marker for quantitative analysis of rDNA organization in Schizosaccharomyces pombe.
GapR-GFP marks overtwisted DNA and can be used to study rDNA morphology:
GapR is a protein that binds to overtwisted DNA. It recruits a topoisomerase to release topological stress on DNA during transcription.
When tagged with GFP, it functions as a fluorescent marker and tracker (live cell imaging) of overtwisted DNA.
To identify overtwisted rDNA specifically, you can tag the nucleolus with a separate color and look at the merged fluorescent images of the nucleolus and overtwisted DNA. Alternatively, you could attach a nuclear localization sequence to GapR-GFP to primarily express it in the nucleus, increasing the probability of only marking rDNA.
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Author response:
The following is the authors’ response to the original reviews
Public Reviews:
Reviewer #1 (Public Review):
Summary:
In the manuscript entitled "Rtf1 HMD domain facilitates global histone H2B monoubiquitination and regulates morphogenesis and virulence in the meningitis-causing pathogen Cryptococcus neoformans" by Jiang et al., the authors employ a combination of molecular genetics and biochemical approaches, along with phenotypic evaluations and animal models, to identify the conserved subunit of the Paf1 complex (Paf1C), Rtf1, and functionally characterize its critical roles in mediating H2B monoubiquitination (H2Bub1) and the consequent regulation of gene expression, fungal development, and virulence traits in C. deneoformans or C. neoformans. Specially, the authors found that the histone modification domain (HMD) of Rtf1 is sufficient to promote H2B monoubiquitination (H2Bub1) and the expression of genes related to fungal mating and filamentation, and restores the fungal morphogenesis and pathogenicity defects caused by RTF1 deletion.
Strengths:
The manuscript is well-written and presents the findings in a clear manner. The findings are interesting and contribute to a better understanding of Rtf1-mediated epigenetic regulation of fungal morphogenesis and pathogenicity in a major human fungal pathogen, and potentially in other fungal species, as well.
Weaknesses:
A major limitation of this study is the absence of genome-wide information on Rtf1-mediated H2B monoubiquitination (H2Bub1), as well as a lack of detail regarding the function of the Plus3 domain. Although overexpression of HMD in the rtf1Δ mutant restored global H2Bub1 levels, it did not rescue certain critical biological functions, such as growth at 39 °C and melanin production (Figure 4C-D). This suggests that the precise positioning of H2Bub1 is essential for Rtf1's function. A comprehensive epigenetic landscape of H2Bub1 in the presence of HMD or full-length Rtf1 would elucidate potential mechanisms and shed light on the function of the Plus3 domain.
We thank the reviewer (and other reviewers) for this excellent suggestion. We have conducted CUT&Tag assays with WT, _rtf1_Δ mutant, and complementary strains with the full length Rtf1 and only HMD domain cultured under 30 and 39 °C. We indeed found that the epigenetic landscape of H2Bub1 in the presence of HMD or full-length Rtf1 has variations. This results strongly suggest that the distribution of H2Bub1 is regulated by Rtf1, and H2B modifications at specific loci in the chromosome may contribute to thermal tolerance in C. neoformans. These new findings from CUT&Tag assays shed lights on understanding the mechanism of thermal tolerance, and we decided not to include these results in the current manuscript.
Reviewer #2 (Public Review):
Summary:
The authors set out to determine the role of Rtf1 in Cryptococcal biology, and demonstrate that Rtf1 acts independently of the Paf1 complex to exert regulation of Histone H2B monoubiquitylation (H2Bub1). The biological impact of the loss of H2Bub1 was observed in defects in morphogenesis, reduced production of virulence factors, and reduced pathogenic potential in animal models of cryptococcal infection.
Strengths:
The molecular data is quite compelling, demonstrating that the Rtf1-depednent functions require only this histone modifying domain of Rtf1, and are dependent on nuclear localization. A specific point mutation in a residue conserved with the Rtf1 protein in the model yeast demonstrates the conservation of that residue in H2Bub1 modification. Interestingly, whereas expression of the HMD alone suppressed the virulence defect of the rtf1 deletion mutant, it did not suppress defects in virulence factor production.
Weaknesses:
The authors use two different species of Cryptococcus to investigate the biological effect of Rtf1 deletion. The work on morphogenesis utilized C. deneoformans, which is well-known to be a robust mating strain. The virulence work was performed in the C. neoformans H99 background, which is a highly pathogenic isolate. The study would be more complete if each of these processes were assessed in the other strain to understand if these biological effects are conserved across the two species of Cryptococcus. H99 is not as robust in morphogenesis, but reproducible results assessing mating and filamentation in this strain have been performed. Similarly, C. deneoformans does produce capsule and melanin.
We thank the reviewer for the suggestion. We have conducted assays to quantify both capsule and melanin production in both C. neoformans and C. deneoformans strain background. We found that capsule production was affected in the same pattern in these two serotypes. Interestingly, we found the cell size was significantly affected by deletion of RTF1 in both serotypes. In addition, melanin production was reduced due to the deletion of RTF1 in both serotypes; However, complementation with Plus3 or mutated alleles of HMD gave different phenotypes in these two serotypes. These new findings were included Figure 4 in the revised manuscript.
There are some concerns with the conclusions related to capsule induction. The images reported in Figure B are purported to be grown under capsule-inducing conditions, yet the H99 panel is not representative of the induced capsule for this strain. Given the lack of a baseline of induction, it is difficult to determine if any of the strains may be defective in capsule induction. Quantification of a population of cells with replicates will also help to visualize the capsular diversity in each strain population.
We thank the reviewer for raising this concern. We have tested capsule production under capsule-inducing condition on 10% fetal bovine serum (FBS) agar medium [1]. Under this condition, the capsule layers surrounding the cells were obvious. We also included noncapsule-producing control in our assay to help the visualization of capsule. In addition, we quantified the ratio between diameters of capsule layer and cell body to show the capsular diversity in each strain population. The results were included in the Figure 4 in the revised manuscript.
The authors demonstrate that for specific mating-related genes, the expression of the HMD recapitulated the wild-type expression pattern. The RNA-seq experiments were performed under mating conditions, suggesting specificity under this condition. The authors raise the point in the discussion that there may be differences in Rtf1 deposition on chromatin in H99, and under conditions of pathogenesis. The data that overexpression of HMD restores H2Bub1 by western is quite compelling, but does not address at which promoters H2Bub1 is modulating expression under pathogenesis conditions, and when full-length Rtf1 is present vs. only the HMD.
We thank the reviewer for raising these concerns. Please see our response to Reviewer #1.
Reviewer #3 (Public Review):
Summary:
In this very comprehensive study, the authors examine the effects of deletion and mutation of the Paf1C protein Rtf1 gene on chromatin structure, filamentation, and virulence in Cryptococcus.
Strengths:
The experiments are well presented and the interpretation of the data is convincing.
Weaknesses:
Yet, one can be frustrated by the lack of experiments that attempt to directly correlate the change in chromatin structure with the expression of a particular gene and the observed phenotype. For example, the authors observed a strong defect in the expression of ZNF2, a known regulator of filamentation, mating, and virulence, in the rtf1 mutant. Can this defect explain the observed phenotypes associated with the RTF1 mutation? Is the observed defect in melanin production associated with altered expression of laccase genes and altered chromatin structure at this locus?
We completely agree with the reviewer. We have conducted CUT&Tag assay, and checked the Rtf1-mediated H2Bub1 at these particular gene loci. We found that the distribution of H2Bub1 at the promoter region of ZNF2 and the gene body of laccase-encoding gene varied possibly due to RTF1 mutation. We would like to save those preliminary findings for another story and not to include in this manuscript as we mentioned in the response to Reviewer #1.
(1) Jang, E.-H., et al., Unraveling Capsule Biosynthesis and Signaling Networks in Cryptococcus neoformans. Microbiology Spectrum, 2022. 10(6): p. e02866-22.
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Author response:
The following is the authors’ response to the original reviews
Reviewer #1 (Public Review):
(1) The rationale for performing genomics, transcriptional, and proteomics work in 293T cells is not discussed. Further, there are no functional readouts mentioned in the 293T cells with expression of the fusion-oncogenes. Did these cells have any phenotypes associated with fusion-oncogene expression (proliferation differences, morphological changes, colony formation capacity)? Further, how similar are the gene expression signatures from RNA-seq to rhabdomyosarcoma? This would help the reader interpret how similar these cell models are to human disease.
We appreciate the reviewer’s comments and understand the limitation of HEK293T cell culture. HEK293T cells were used as a surrogate system that enabled us to systemically examine and compare the transcriptional activation mechanisms between VGLL2-NCOA2/TEAD1-NCOA2 and YAP/TAZ. HEK293T cells have previously been used as a model system to study the signaling and transcriptional mechanisms of the Hippo/YAP pathway (1,2). Our data also showed that the ectopic expression of VGLL2-NCOA2 and TEAD1-NCOA2 in HEK293 cells can promote proliferation (Figure 1-figure supplement 1B), consistent with their potential oncogenic function.
(2) TEAD1::NCOA2 fusion-oncogene model was not credentialed past H&E, and expression of Desmin. Is the transcriptional signature in C2C12 or 293T similar to a rhabdomyosarcoma gene signature?
We understand the reviewer’s concern. VGLL2-NCOA2 in vivo tumorigenesis model generated by C2C12 cell orthotopic transplantation has recently been reported, and it exhibits similar characteristics with zebrafish transgenic tumors as well as human scRMS samples that carry the VGLL2-NCOA2 fusion (3). Due to the similar transcriptional and oncogenic mechanisms employed by both VGLL2-NCOA2 and TEAD1-NCOA2 fusion proteins, we expect that the TEAD1-NCOA2 dependent C2C12 transplantation model will closely resemble that induced by VGLL2-NCOA2.
(3) For the fusion-oncogenes, did the HA, FLAG, or V5 tag impact fusion-oncogene activity? Was the tag on the 3' or 5' of the fusion? This was not discussed in the methods.
To address the reviewer’s concern, we carefully compared the transcriptional activity of the fusion proteins with the HA tag at the 5’ end or FLAG and V5 tag at the 3’ end. We found that neither the tag type nor its location significantly affects the ability of VGLL2-NCOA2 and TEAD1-NCOA2 to induce downstream gene transcription, measured by qPCR. The data is summarized in Figure 1-figure supplement 1 G-H.
(4) Generally, the lack of details in the figures, figure legends, and methods make the data difficult to interpret. A few examples are below:
a. Individual data points are not shown for figure bar plots (how many technical or biological replicates are present and how many times was the experiment repeated?).
As requested, we have added the individual data points to the bar plots. The Method section now includes information on the number of biological replicates and the times the experiments were repeated.
b. What exons were included in the fusion-oncogenes from VGLL2 and NCOA2 or TEAD1 and NCOA2?
We have now included the exon structure organization of VGLL2-NCOA2 or TEAD1-NCOA2 fusions in Figure 1-figure supplement 1A.
c. For how long were the colony formation experiments performed? Two weeks?
We have included more detailed information about the colony formation assay in the Methods section.
d. In Figure 2D, what concentration of CP1 was used and for how long?
The CP1 concentration and treatment duration information has now been included in the figure legend and Methods section.
e. How was A485 resuspended for cell culture and mouse experiments, what is the percentage of DMSO?
The Methods section now includes detailed information on how A485 is prepared for in vitro and in vivo experiments.
f. How many replicates were done for RNA-seq, CUT&RUN, and ATACseq experiments?
RNA-seq was done with three biological replicates and CUT&RUN and ATAC-seq were performed with two biological replicates. This information is now included in the Methods section for clarification.
Reviewer #2 (Public Review):
In the manuscript entitled "VGLL2 and TEAD1 fusion proteins drive YAP/TAZ-independent transcription and tumorigenesis by engaging p300", Gu et al. studied two Hippo pathway-related gene fusion events (i.e., VGLL2-NCOA2, TEAD1-NCOA2) in spindle cell rhabdomyosarcoma (scRMS) and showed that their fusion proteins can activate Hippo downstream gene transcription independent of YAP/TAZ. Using the BioID-based mass spectrometry analysis, the authors revealed histone acetyltransferase CBP/p300 as specific binding proteins for VGLL2-NCOA2 and TEAD1-NCOA2 fusion proteins. Pharmacologically targeting p300 inhibited the fusion proteins-induced Hippo downstream gene transcription and tumorigenic events.
Overall, this study provides mechanistic insights into the scRMS-associated gene fusions in tumorigenesis and reveals potential therapeutic targets for cancer treatment. The manuscript is well-written and easy to follow.
Here, several suggestions are made for the authors to improve their study.
Main points
(1) The authors majorly focused on the Hippo downstream gene transcription in this study, while a significant portion of genes regulated by the VGLL2-NCOA2 and TEAD1-NCOA2 fusion proteins are non-Hippo downstream genes (Figure 3). The authors should investigate whether the altered Hippo pathway transcription is essential for VGLL2-NCOA2 and TEAD1-NCOA2-induced cell transformation and tumorigenesis. Specifically, they should test if treatment with the TEAD inhibitor can reverse the cell transformation and tumorigenesis caused by VGLL2-NCOA2 but not TEAD1-NCOA2. In addition, it is important to examine whether YAP-5SA expression can rescue the inhibitory effects of A485 on VGLL2-NCOA2 and TEAD1-NCOA2-induced colony formation and tumor growth. This will help clarify whether Hippo downstream gene transcription is important for the oncogenic activities of these two fusion proteins.
We thank the reviewer for the comments. Although we have not tested the small molecular TEAD inhibitor on VGLL2-NCOA2 or TEAD1-NCOA2-induced cell transformation and tumorigenesis, we expect that TEAD inhibition will block VGLL2-NCOA2- but not TEAD1-NCOA2-induced oncogenic activity. It is because TEAD1-NCOA2 does not contain the auto-palmitoylation sites and the hydrophobic pocket in the C-terminal YAP-binding domain of TEAD1 that the TEAD small molecule inhibitor occupies (4). We also appreciate the reviewer’s suggestion of YAP5SA rescue experiments. However, due to its strong oncogenic activity, YAP5SA itself can induce robust downstream transcription and cell transformation with or without A485 treatment, as shown in Figure 5. Thus, it will be unlikely to address whether non-Hippo downstream genes induced by the fusions are important for cell transformation and tumorigenesis. Because of the distinct nature of transcriptional and chromatin landscapes controlled by VGLL2-NCOA2/TEAD-NCOA2 and YAP, we speculate that both Hippo and non-Hippo-related downstream genes contribute to the oncogenic activation and tumor phenotypes induced by the fusion proteins.
(2) Rationale for selecting CBP/p300 for functional studies needs to be provided. The BioID-MS experiment identified many interacting proteins for VGLL2-NCOA2 and TEAD1-NCOA2 fusion proteins (Table S4). The authors should explain the scoring system used to identify the high-interacting proteins for VGLL2-NCOA2 and TEAD1-NCOA2 fusion proteins. Was CEP/p300 the top candidates on the list? Providing this information will help justify the focus on CBP/p300 and validate their importance in this study.
We appreciate the reviewer’s point. CBP/P300 is among the top hits in our proteomics screens of both VGLL2-NCOA2 and TEAD1-NCOA2. Our focus on CBP/P300 is mainly due to the well-established interactions between CBP/P300 and the NCOA family transcriptional co-activators, in which the CBP/P300-NCOA complex plays a central role in mediating nuclear receptors-induced transcriptional activation (5). In addition, our data is consistent with another re-current Vgll2 fusion identified in scRMS, VGLL2-CITED2 (6) that has a C-term fusion partner from CITED2, which is a known CBP/P300 interacting protein (7).
(3) p300 was revealed as a key driver for the VGLL2-NCOA2 and TEAD1-NCOA2 fusion proteins-induced transcriptome alteration and tumorigenesis. To strengthen the point, the authors should identify the p300 binding region on VGLL2-NCOA2 and TEAD1-NCOA2 fusion proteins. Mutants with defects in p300 binding/recruitment should be generated and included as a control in the related q-PCR and tumorigenic studies. This work will help confirm the crucial role of p300 in mediating the oncogenic effects of these two fusion proteins.
We thank the reviewer for the suggestion. We have performed the co-immunoprecipitation assay using the deletion mutant form of VGLL2-NCOA2. We have performed additional co-immunoprecipitation experiments and demonstrated that the C-term NCOA2 part of the fusion is responsible for mediating the interaction between the fusion protein and CBP/P300. These results are now included in the new Figure 5A and are consistent with the reported structural analysis of CBP/P300-NCOA complex (8). In addition, our new data showed the inability of the VGLL2-NCOA2 ∆NCOA2 mutant to induce gene transcription (Figure 1-figure supplement 1D). Furthermore, our data using the small molecular CBP/P300 inhibitor clearly demonstrated that CBP/P300 is required to mediate cell transformation and tumorigenesis induced by the two fusion proteins in vitro and in vivo (Figure 5 and 6).
(4) Another major issue is the overexpression system extensively used in this study. It is important to determine whether the VGLL2-NCOA2 and TEAD1-NCOA2 fusion genes are also amplified in cancer. If not, the expression levels of the VGLL2-NCOA2 and TEAD1-NCOA2 fusion proteins should be adjusted to endogenous levels to assess their oncogenic effects on gene transcription and tumorigenesis. This approach would make the study more relevant to the pathological conditions observed in scRMS cancer patients.
We appreciate the reviewer’s input and acknowledge the limitation of the HEK293T and C2C12 cell-based models that rely on ectopic expression of VGLL2-NCOA2 and TEAD1-NCOA2 fusion proteins. It is currently unclear whether the VGLL2-NCOA2 and TEAD1-NCOA2 fusion genes are also amplified in sarcoma. As mentioned before, these surrogate cell culture systems allowed us to systemically compare the transcriptional regulation by the fusion proteins and YAP/TAZ and elucidate the molecular mechanism underlying the Hippo/YAP-independent oncogenic transformation induced by VGLL2-NCOA2 and TEAD1-NCOA2.
References:
(1) Genes Dev . 2007 Nov 1;21(21):2747-61. doi: 10.1101/gad.1602907. Inactivation of YAP oncoprotein by the Hippo pathway is involved in cell contact inhibition and tissue growth control
(2) Genes Dev . 2010 Jan 1;24(1):72-85. doi: 10.1101/gad.1843810. A coordinated phosphorylation by Lats and CK1 regulates YAP stability through SCF(beta-TRCP)
(3) VGLL2-NCOA2 leverages developmental programs for pediatric sarcomagenesis. Watson S, LaVigne CA, Xu L, Surdez D, Cyrta J, Calderon D, Cannon MV, Kent MR, Cell Rep. 2023 Jan 31;42(1):112013.
(4) Lats1/2 Sustain Intestinal Stem Cells and Wnt Activation through TEAD-Dependent and Independent Transcription. Cell Stem Cell. 2020 May 7;26(5):675-692.e8.
(5) Yi, P., Yu, X., Wang, Z., and O’Malley, B.W. (2021). Steroid receptor-coregulator transcriptional complexes: new insights from CryoEM. Essays Biochem. 65, 857–866.
(6) A Molecular Study of Pediatric Spindle and Sclerosing Rhabdomyosarcoma: Identification of Novel and Recurrent VGLL2-related Fusions in Infantile Cases. Am J Surg Pathol . 2016 Feb;40(2):224-35. doi: 10.1097/
(7) CITED2 and the modulation of the hypoxic response in cancer. Fernandes MT, Calado SM, Mendes-Silva L, Bragança J.World J Clin Oncol. 2020 May 24;11(5):260-274.
(8) Yu, X., Yi, P., Hamilton, R.A., Shen, H., Chen, M., Foulds, C.E., Mancini, M.A., Ludtke, S.J., Wang, Z., and O’Malley, B.W. (2020). Structural insights of transcriptionally active, full-length Androgen receptor coactivator complexes. Mol. Cell 79, 812–823.e4.
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Reviewer #3 (Public review):
Summary
This work investigated the immune response in the murine retina after focal laser lesions. These lesions are made with close to 2 orders of magnitude lower laser power than the more prevalent choroidal neovascularization model of laser ablation. Histology and OCT together show that the laser insult is localized to the photoreceptors and spares the inner retina, the vasculature and the pigment epithelium. As early as 1-day after injury, a loss of cell bodies in the outer nuclear layer is observed. This is accompanied by strong microglial proliferation to the site of injury in the outer retina where microglia do not typically reside. The injury did not seem to result in the extravasation of neutrophils from the capillary network, constituting one of the main findings of the paper. The demonstrated paradigm of studying the immune response and potentially retinal remodeling in the future in vivo is valuable and would appeal to a broad audience in visual neuroscience.
Strengths
Adaptive optics imaging of murine retina is cutting edge and enables non-destructive visualization of fluorescently labeled cells in the milieu of retinal injury. As may be obvious, this in vivo approach is a benefit for studying fast and dynamic immune processes on a local time scale - minutes and hours, and also for the longer days-to-months follow-up of retinal remodeling as demonstrated in the article. In certain cases, the in vivo findings are corroborated with histology.
The analysis is sound and accompanied by stunning video and static imagery. A few different sets of mouse models are used, a) two different mouse lines, each with a fluorescent tag for neutrophils and microglia, b) two different models of inflammation - endotoxin-induced uveitis (EAU) and laser ablation are used to study differences in the immune interaction.
One of the major advances in this article is the development of the laser ablation model for 'mild' retinal damage as an alternative to the more severe neovascularization models. This model would potentially allow for controlling the size, depth and severity of the laser injury opening interesting avenues for future study.
The time-course, 2D and 3D spatial activation pattern of microglial activation are striking and provide an unprecedented view of the retinal response to mild injury.
Weaknesses
Generalization of the (lack of) neutrophil response to photoreceptor loss - there is ample evidence in literature that neutrophils are heavily recruited in response to severe retinal damage that includes photoreceptor loss. Why the same was not observed here in this article remains an open question. One could hypothesize that neutrophil recruitment might indeed occur under conditions that are more in line with the more extreme damage models, for example, with a stronger and global ablation (substantially more photoreceptor loss over a larger area). This parameter space is unwieldy and sufficiently large to address the question conclusively in the current article, i.e. how much photoreceptor loss leads to neutrophil recruitment? By the same token, the strong and general conclusion in the title - Photoreceptor loss does not recruit neutrophils - cannot be made until an exhaustive exploration be made of the same parameter space. A scaling back may help here, to reflect the specific, mild form of laser damage explored here, for instance - Mild photoreceptor loss does not recruit neutrophils despite...
EIU model - The EIU model was used as a positive control for neutrophil extravasation. Prior work with flow cytometry has shown a substantial increase in neutrophil counts in the EIU model. Yet, in all, the entire article shows exactly 2 examples in vivo and 3 ex vivo (Figure 7) of extravasated neutrophils from the EIU model (n = 2 mice). The general conclusion made about neutrophil recruitment (or lack thereof) is built partly upon this positive control experiment. But these limited examples, especially in the case where literature reports a preponderance of extravasated neutrophils, raise a question on the paradigm(s) used to evaluate this effect in the mild laser damage model.
Overall, the strengths outweigh the weaknesses, provided the conclusions/interpretations are reconsidered.
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Author response:
The following is the authors’ response to the previous reviews
Reviewer #1 (Public review):
Summary:
The authors aimed to investigate the interaction between tissue-resident immune cells (microglia) and circulating systemic neutrophils in response to acute, focal retinal injury. They induced retinal lesions using 488 nm light to ablate photoreceptor (PR) outer segments, then utilized various imaging techniques (AOSLO, SLO, and OCT) to study the dynamics of fluorescent microglia and neutrophils in mice over time. Their findings revealed that while microglia showed a dynamic response and migrated to the injury site within a day, neutrophils were not recruited to the area despite being nearby. Post-mortem confocal microscopy confirmed these in vivo results. The study concluded that microglial activation does not recruit neutrophils in response to acute, focal photoreceptor loss, a scenario common in many retinal diseases.
Strengths:
The primary strength of this manuscript lies in the techniques employed.
In this study, the authors utilized advanced Adaptive Optics Scanning Laser Ophthalmoscopy (AOSLO) to document immune cell interactions in the retina accurately. AOSLO's micron-level resolution and enhanced contrast, achieved through near-infrared (NIR) light and phase-contrast techniques, allowed visualization of individual immune cells without extrinsic dyes. This method combined confocal reflectance, phase-contrast, and fluorescence modalities to reveal various cell types simultaneously. Confocal AOSLO tracked cellular changes with less than 6 μm axial resolution, while phase-contrast AOSLO provided detailed views of vascular walls, blood cells, and immune cells. Fluorescence imaging enabled the study of labeled cells and dyes throughout the retina. These techniques, integrated with conventional histology and Optical Coherence Tomography (OCT), offered a comprehensive platform to visualize immune cell dynamics during retinal inflammation and injury.
Thank you!
Weaknesses:
One significant weakness of the manuscript is the use of Cx3cr1GFP mice to specifically track GFP-expressing microglia. While this model is valuable for identifying resident phagocytic cells when the blood-retinal barrier (BRB) is intact, it is important to note that recruited macrophages also express the same marker following BRB breakdown. This overlap complicates the interpretation of results and makes it difficult to distinguish between the contributions of microglia and infiltrating macrophages, a point that is not addressed in the manuscript.
We agree that greater emphasis is required that CX3CR1 mice exhibit fluorescence in not only microglia, but also other cells of macrophage origin including monocytes, perivascular macrophages and some hyalocytes.
Through the advantages of in vivo AOSLO, however, we are able to establish that CX3CR1 cells are present within the tissue before the laser lesion is placed. This suggests they are tissue resident. We agree that it is possible that at later time points (days-weeks), systemic macrophages and/or monocytes may participate. Lack of rolling/crawling cells suggest they are not systemic. We elaborate on this point in a new section in the discussion:
P29 L534-541:
“CX3CR1-GFP mice exhibit fluorescence not only in microglia
We recognize that the CX3CR1-GFP model can also label systemic cells such as monocytes/macrophages77. While it is possible these cells could infiltrate the retina in response to the lesion, we find it unlikely since there was no indication of the leukocyte extravasation cascade (rolling/crawling/stalled cells) within the nearest retinal vasculature. In addition to microglia, retinal perivascular macrophages and hyalocytes also exhibit GFP fluorescence and thus that these cells may also contribute toward damage resolution.”
Another major concern is the time point chosen for analyzing the neutrophil response. The authors assess neutrophil activity 24 hours after injury, which may be too late to capture the initial inflammatory response. This delayed assessment could overlook crucial early dynamics that occur shortly after injury, potentially impacting the overall findings and conclusions of the study.
The power of in vivo imaging makes these early assessments possible. Therefore, we have taken the reviewers concern and conducted an additional experiment which examines whether neutrophils are seen in the window of time between lesion and 24hrs. In a newly examined mouse, we find that within 3.5 hours post-lesion, neutrophils do not extravasate adjacent to the lesion site (see new “figure 8 – figure supplement 1”).
Also see accompanying video (new “figure 8 – video 3”) for an example of nearby neutrophils flowing through OPL capillaries just microns away from the lesion site. Neutrophils are clearly contained within the vasculature and exhibit dynamics consistent with healthy retinal tissue. While it remains possible that the lesion may increase leukocyte stalling within the nearest capillaries, we are unable to confirm or deny this with a single experiment. We now submit this evidence as a new supplementary figure following the reviewer’s suggestion.
Reviewer #2 (Public review):
Summary:
This study uses in vivo multimodal high-resolution imaging to track how microglia and neutrophils respond to light-induced retinal injury from soon after injury to 2 months post-injury. The in vivo imaging finding was subsequently verified by an ex vivo study. The results suggest that despite the highly active microglia at the injury site, neutrophils were not recruited in response to acute light-induced retinal injury.
Strengths:
An extremely thorough examination of the cellular-level immune activity at the injury site. In vivo imaging observations being verified using ex vivo techniques is a strong plus.
We appreciate this recognition and hope that the reviewer considers the weaknesses below in the context of the papers identified strengths.
Weaknesses:
This paper is extremely long, and in the perspective of this reviewer, needs to be better organized.
We agree and have taken the following steps to address this:
(1) Paper has been shortened overall by 8%
(2) We reorganized the following sections:
a. Introduction: shortened
b. Methods: merged section “Ex vivo confocal image processing” with “Ex vivo confocal imaging”.
c. Results: most sections shortened, others simplified for concision
d. Discussion: most sections shortened, removed “Microglial/neutrophil discrimination using label-free phase contrast”
e. Figure references reorganized in order of their appearance.
Study weakness: though the finding prompts more questions and future studies, the findings discussed in this paper are potentially important for us to understand how the immune cells respond differently to different severity levels of injury.
On the heels of this burgeoning technology, we consider this report among the first studies of its kind. We are hopeful that it forms the foundation of many further investigations to come. We expect a rich parameter space to be explored with future studies including investigation of other time points, other injuries of varying degree and other immune cell populations (along with their interactions with each other). Each has the potential to reveal the complexities of the ocular immune system in action.
Reviewer #3 (Public review):
Summary:
This work investigated the immune response in the murine retina after focal laser lesions. These lesions are made with close to 2 orders of magnitude lower laser power than the more prevalent choroidal neovascularization model of laser ablation. Histology and OCT together show that the laser insult is localized to the photoreceptors and spares the inner retina, the vasculature, and the pigment epithelium. As early as 1-day after injury, a loss of cell bodies in the outer nuclear layer is observed. This is accompanied by strong microglial proliferation at the site of injury in the outer retina where microglia do not typically reside. The injury did not seem to result in the extravasation of neutrophils from the capillary network constituting one of the main findings of the paper. The demonstrated paradigm of studying the immune response and potentially retinal remodeling in the future in vivo is valuable and would appeal to a broad audience in visual neuroscience. However, there are some issues with the conclusions drawn from the data and analysis that can be addressed to further bolster the manuscript.
Strengths:
Adaptive optics imaging of the murine retina is cutting edge and enables non-destructive visualization of fluorescently labeled cells in the milieu of retinal injury. As may be obvious, this in vivo approach is beneficial for studying fast and dynamic immune processes on a local time scale - minutes and hours, and also for the longer days-to-months follow-up of retinal remodeling as demonstrated in the article. In certain cases, the in vivo findings are corroborated with histology.
Thank you!
The analysis is sound and accompanied by stunning video and static imagery. A few different sets of mouse models are used, (a) two different mouse lines, each with a fluorescent tag for neutrophils and microglia, (b) two different models of inflammation - endotoxin-induced uveitis (EAU) and laser ablation are used to study differences in the immune interaction.
Thank you!
One of the major advances in this article is the development of the laser ablation model for 'mild' retinal damage as an alternative to the more severe neovascularization models. While not directly shown in the article, this model would potentially allow for controlling the size, depth, and severity of the laser injury opening interesting avenues for future study.
We agree that there is an established community that is invested in developing titrated dosimetry for light damage models. As the reviewer recognizes, this parameter space is exceptionally large therefore we controlled this parameter by choosing a single wavelength that is commonly used in ophthalmoscopy (488nm), fixed duration and exposure regime that created a reproducible, mild damage of photoreceptors. At this titration we created a mild lesion that spares retina above and below.
Weaknesses:
(1) It is unclear based on the current data/study to what extent the mild laser damage phenotype is generalizable to disease phenotypes. The outer nuclear cell loss of 28% and a complete recovery in 2 months would seem quite mild, thus the generalizability in terms of immune-mediated response in the face of retinal remodeling is not certain, specifically whether the key finding regarding the lack of neutrophil recruitment will be maintained with a stronger laser ablation.
It seems the concern here is whether our finding is generalizable to other damage regimes, especially more severe ones. While speculative, we would suspect that it is not generalizable across different lesions of greater severity. For example, puncturing Bruch’s membrane is an example of a more severe phenotype that is often encountered in laser damage. However, this creates a complicated model that not only induces inflammation, but also compromises BRB integrity and promotes CNV. The parameter space to be tested in the reviewer’s question is quite vast and therefore have tried to summarize the generalizability within our manuscript in
P31 L586-588 “There are limitations on how generalizable this mild damage to more severe damage or disease phenotypes, but this acute damage model can begin to provide clues about how immune cells interact in response to PR loss. In this laser lesion model, we ablate 27% of the PRs in a 50 µm region.”
(2) Mice numbers and associated statistics are insufficient to draw strong conclusions in the paper on the activity of neutrophils, some examples are below:
a) 2 catchup mice and 2 positive control EAU mice are used to draw inferences about immune-mediated activity in response to injury. If the goal was to show 'feasibility' of imaging these mouse models for the purposes of tracking specific cell type behavior, the case is sufficiently made and already published by the authors earlier. It is possible that a larger sample size would alter the conclusion.
We would like to highlight that the total number of mice studied in this report was 28 (18 in-vivo imaging, 10 ex-vivo histology, >40 lesions total). While power analysis is challenging as these are the first studies of their kind, we underscore that in vivo imaging allows those same mice to be studied multiple times longitudinally. This is not possible with traditional histology. Therefore, in vivo imaging not only reveals the temporal progression (unlike histology), but also increases the number of observations beyond a simple count of the “number of mice”.
The goal of the study was not one of feasibility. The goal was to address a specific question in ocular biology: “do resident CX3CR1 cells recruit neutrophils in early, regional retinal injury”
The low numbers that the reviewer points to, are not the primary data of the paper, rather, supportive control data. Moreover, we refocus the attention on the fact that our study is performed on 28 mice across multiple modalities and each corroborates a common finding that neutrophils do not appear to be recruited despite strong microglial response; a central finding of the paper.
b) There are only 2 examples of extravasated neutrophils in the entire article, shown in the positive control EAU model. With the rare extravasation events of these cells and their high-speed motility, the chance of observing their exit from the vasculature is likely low overall, therefore the general conclusions made about their recruitment or lack thereof are not justified by these limited examples shown.
The spirit of the challenge raised is that because nothing was seen, is not proof that nothing occurred. Said more commonly, “absence of evidence is not evidence of absence”- a quote often attributed to Carl Sagan. Yet we push back on this conjecture as we have shown, not only with cutting edge in vivo imaging, but also with ample histological controls as well as multiple transgenic animals (and corroborating IHC antibodies) that in none of these imaging modalities, at none of the time points we evaluated, did neutrophils aggregate or extravasate in response to photoreceptor ablation.
Reviewer adds: “the chance of observing their exit from the vasculature is likely low overall…”
This is the reason that we specifically chose a focal lesion model to increase any possible chance of imaging a rare event. The focal lesion provides both a time and a location for “where” to look. Small 50 micrometer lesions were sufficient to drive a strong local microglial response (figures 5,6,9). This was evidence that local inflammatory cues were present. Yet despite this activation, neutrophils were not recruited to this location. We emphasize that this is a strength of our approach over other pan-retinal damage models that may indeed miss the rare extravasation events that are geographically sparse and happen over hours.
c) In Figure 3, the 3-day time point post laser injury shows an 18% reduction in the density of ONL nuclei (p-value of 0.17 compared to baseline). In the case of neutrophils, it is noted that "Control locations (n = 2 mice, 4 z-stacks) had 15 {plus minus} 8 neutrophils per sq.mm of retina whereas lesioned locations (n = 2 mice, 4 z-stacks) had 23 {plus minus} 5 neutrophils per sq.mm of retina (Figure 10b). The difference between control and lesioned groups was not statistically significant (p = 0.19)." These data both come from histology. While the p-values - 0.17 and 0.19 - are similar, in the first case a reduction in ONL cell density is concluded while in the latter, no difference in neutrophil density is inferred in the lesioned case compared to control. Why is there a difference in the interpretation where the same statistical test and methodology are used in both cases? Besides this statistical nuance, is there an alternate possibility that there is an increased, albeit statistically insignificant, concentration of circulating neutrophils in the lesioned model? The increase is nearly 50% (15 {plus minus} 8 vs. 23 {plus minus} 5 neutrophils per sq.mm) and the reader may wonder if a larger animal number might skew the statistic towards significance.
The statistics and p-values will be dependent on the strategy of analysis performed. As described in the methods, we used a predetermined 50 micron cylinder for our counting analysis based on the average lesion size created. We used this circular window to roughly approximate the size of the common lesion size. However, recall that the damage is created in a single axis (a line projected on the retina) therefore it is possible that the analysis region is too generous to capture the exceptionally local damage.
While the reviewer is focused on the nuance of statistics, we would like to refocus the conversation on our data that shows that very few neutrophils were observed at all (105 cells from 8 locations, P value reported). But missed in the above critique is that all neutrophils were contained within capillaries (Fig 10). We found no examples of extravasated neutrophils. This is the major finding and is supported by our in vivo as well as ex vivo confirmation.
(2) The conclusions on the relative activity of neutrophils and microglia come from separate animals. The reader may wonder why simultaneous imaging of microglia and neutrophils is not shown in either the EAU mice or the fluorescently labeled catchup mice where the non-labeled cell type could possibly be imaged with phase-contrast as has been shown by the authors previously. One might suspect that the microglia dynamics are not substantially altered in these mice compared to the CX3CR1-GFP mice subjected to laser lesions, but for future applicability of this paradigm of in vivo imaging assessment of the laser damage model, including documenting the repeatability of the laser damage model and the immune cell behavior, acquiring these data in the same animals would be critical.
A double fluorescent mouse (neutrophils and microglia) is a logical next step of this research. In fact, we have now crossed these transgenic mice and are studying this double labeled mouse in a second manuscript in preparation. However, for this study, it was imperative that the fluorescent imaging light was kept at low levels as not to contribute or alter the lesion phenotype and accompanying immune response. Therefore, imaging two fluorescent channels to simultaneously view neutrophils and microglia in the same animal would have required at least 2X the visible light exposure for imaging. The imaging light levels used in the current study were carefully examined in our previous publications as to not create additional light damage (Joseph et al 2021).
(3) Along the same lines as above, the phase contrast ONL images at time points from 3-day to 2-month post laser injury are not shown and the absence of this data is not addressed. This missing data pertains only to the in vivo imaging mice model but are conducted in histology that adequately conveys the time-course of cell loss in the ONL.
The ocular preparation of the phase contrast data in figure 2, unfortunately developed an anesthesia induced cataract that precluded adequate image quality. This is not uncommon in long-term mouse ocular imaging preparations (Feng et al 2023). Instead, we chose to include the phase-contrast data to show the visually compelling intact and disrupted ONL damage for baseline and 1 day to show that the damage is not only focal, but also shows clear disruption to the somatic layers of the photoreceptors.
It is suggested that the reason be elaborated for the exclusion of this data and the simultaneous imaging of microglia and neutrophils mentioned above.
We agree and we have included the reason for the “not acquired” data within the figure 2 legend:
“Phase contrast data was not acquired for time points 3 days-2 months due to development of cataract which obscured the phase contrast signal”
Also, it would be valuable to further qualify and check the claims in the Discussion that "ex vivo analysis confirms in vivo findings" and "Microglial/neutrophil discrimination using label-free phase contrast"
We maintain that ex vivo analysis both corroborates and in many cases, confirms our in vivo findings. We feel this is a strength of our manuscript rather than a qualifier. A) Damage localization is visible with OCT and confocal/phase contrast AOSLO in a region that matches the DAPI loss we see ex vivo. B) Disruption of the ONL seen with in vivo AOSLO is of the same size, shape and location as the ONL damage quantified ex vivo. C) No damage or disruption was seen in locations above the lesion with OCT or AOSLO, which matches our finding that only the ONL shows loss of nuclei whereas other more superficial layers are spared. D) Microglial localization is found both in vivo and ex vivo and E) lack of neutrophil aggregation or extravasation was neither seen in vivo or ex vivo. Given the evidence above, we contend that this strong synergistic and complementary approach corroborates the experimental data in two ways of studying this tissue.
We agree that the claims made in the section entitled “Microglial/neutrophil discrimination using label-free phase contrast” are not strongly supported by the phase-contrast imaging presented in this paper. Accordingly, we have since removed this section based on reviewer suggestion.
Recommendations for the authors:
Reviewer #1 (Recommendations for the authors):
(1) Based on the title and abstract, the main focus of the manuscript appears to be the immune response. However, most of the manuscript is dedicated to the authors' imaging technique. Additionally, several important concerns regarding the investigation of the immune response in the retina need to be addressed.
We understand that emphasis may appear to be on the imaging technique, however, because AOSLO is not a widely used technology, we are committed to explaining the technique so that it both builds awareness and confidence in the way this exciting new data is acquired.
(2) The authors indicate '1 day post-injury' as a timeframe spanning between 18 and 28 hours post-injury. This is a rather wide window of time, which could potentially affect the analysis. It is necessary to demonstrate that there is no significant difference in the immune response, particularly in terms of microglial morphology and branch orientation, between 18 and 28 hours post-injury.
We agree that a fine time scale may show even greater insight to the natural history of the inflammatory response. However, we feel that our chosen time points go above and beyond the temporal precision that is offered by other investigations, especially considering the novel multi-modal imaging performed here. Studies using finer temporal sampling are poised for future investigation.
(3) The authors should consider using additional markers or complementary techniques to differentiate between microglia and recruited macrophages, such as incorporating immunohistochemistry with P2RY12, a specific marker for microglia that helps distinguish them from macrophages, and CD68 or F4/80, markers for recruited macrophages. It is also crucial for the authors to include a discussion addressing the limitations of using Cx3cr1GFP mice and the potential impact on result interpretation. It is fundamental to validate the findings and clarify the roles of microglia and macrophages.
The wonders of current IHC is that there are myriad antibodies and labels that “could” be used. We used what we felt were the most compelling for this stage of early investigation. We look forward to studies that employ this wider range of labels. See our response to reviewer 1’s first comment above for addressing the limitations of using Cx3CR1 mice.
(4) Analyzing neutrophil responses at 24 hours post-injury may be too late to capture the critical early dynamics of inflammation. By this time, the initial recruitment and activation phases of neutrophils may have already peaked or begun to resolve, potentially missing key insights into the immediate immune response. The authors should conduct additional analysis of neutrophil responses at earlier time points post-injury, such as 6 or 12 hours. Including these time points would provide a more comprehensive and conclusive analysis of the neutrophil response, helping to delineate the progression of inflammation and its implications for subsequent healing processes.
This point has been addressed above. Briefly, we have now included a new experiment (and figure + video) that shows no neutrophil extravasation at earlier time points. We thank the reviewer for this helpful suggestion.
Reviewer #2 (Recommendations for the authors):
This paper is extremely long, and in the perspective of this reviewer, needs to be better organized.
(1) There was a lengthy description and verification of light-induced injury and longitudinal tracking of healing, which I believe can be further cleaned up and made more succinct.
We have cleaned-up and re-organized the manuscript (see above response for details). Manuscript has been reorganized and reduced by 8%.
(2) The intention/goal of the paper can be further strengthened. On page 33: "to what extent do neutrophils respond to acute neural loss in the retina?" This particular statement is so clear and really brings out the purpose of this study, and it will be great to see something like this in the opening statement.
We thank the reviewer for this excellent suggestion. We have modified the final paragraph of the introduction to strengthen our study’s intention.
P4 L45-47: Here, we ask the question: “To what extent do microglia/neutrophils respond to acute neural loss in the retina?” To begin unraveling the complexities in this response, we deploy a deep retinal laser ablation model.
(3) The figures are not mentioned in the manuscript in the order they were numbered. It makes it extremely challenging to follow along. The methods/results sections started with Figure 1, then on to Figure 4, then back to Figures 2 and 3, etc. This reviewer recommends re-organizing figures and their order of appearance so the contents of the figures are referred to in the paragraph in the most efficient and clear manner.
We have re-organized the appearance of figure references throughout the paper.
(4) Figure 2: phase contrast was not acquired on days 3, 7, and 2 months. Please briefly explain the reason in the caption.
Addressed above.
(5) Figure 4 OPL layer, the area highlighted in a dashed circle was meant to demonstrate that perfusion was intact, but I cannot see the flow in the highlighted area very well at day 7 and 2 months (especially 2 months). Please explain.
Perfusion maps are often difficult to interpret as a static image. Therefore, we have additionally provided the raw video data (“OPL_vasculature_7d” and “OPL_vasculature_2mo”) which helps visualize active perfusion. To the reviewer’s point, videos reveal that RBC motion is maintained in the capillaries of this location.
(6) While there's a thorough discussion of the biological impact of the finding, the uniqueness of the imaging technique can be better highlighted. Immune response toward injury is highly dynamic and is often the first step of wound healing. To observe such dynamic events longitudinally in the living eye at the cellular level, it requires a special imaging technique such as the type addressed here. The author can better address the technical uniqueness of studying this type of biological event for readers less familiar with AOSLO.
We agree and following the reviewer’s suggestion have further emphasized the advance in the current manuscript in two additional places:
(1) Within the introduction
P3-4 L21-42: “A missed window of interaction is highly problematic in histological study where a single time point reveals a snapshot of the temporally complex immune response, which changes dynamically over time. Here, we use in vivo imaging to overcome these constraints.
Documenting immune cell interactions in the retina over time has been challenged by insufficient resolution and contrast to visualize single cells in the living eye. The microscopic size of immune cells requires exceptional resolution for detection. Recently, advances in AOSLO imaging have provided micron-level resolution and enhanced contrast for imaging individual immune cells in the retina and without requiring extrinsic dyes(7,23). AOSLO provides multi-modal information from confocal reflectance, phase-contrast and fluorescence modalities, which can reveal a variety of cell types simultaneously in the living eye. Here, we used confocal AOSLO to track changes in reflectance at cellular scale. Phase-contrast AOSLO provides detail on highly translucent retinal structures such as vascular wall, single blood cells(27–29), PR somata(30), and is well-suited to image resident and systemic immune cells.(7,23) Fluorescence AOSLO provides the ability to study fluorescently-labeled cells(25,31,32) and exogenous dyes(27,33) throughout the living retina. These modalities used in combination have recently provided detailed images of the retinal response to a model of human uveitis.(23,34) Together, these innovations now provide a platform to visualize, for the first time, the dynamic interplay between many immune cell types, each with a unique role in tissue inflammation.”
(2) Within the discussion
P34-35 L656-662 “Beyond the context of this specific finding, we share this work with the excitement that AOSLO cellular level imaging may reveal the interaction of multiple immune cell types in the living retina. By using fluorophores associated with specific immune cell populations, the complex dynamics that orchestrate the immune response may be examined in this specialized tissue. This work and future studies may reveal further insights to the interactions of single immune cells in the living body in a non-invasive way.”
Reviewer #3 (Recommendations for the authors):
Some other comments:
(1) The reader may wonder why if all findings are confirmed by histology would an in vivo imaging model be needed. This does not need a generalized explanation given the typical virtues of an in vivo model, but perhaps the authors may want to amplify their findings in the current context, for example, those on the shorter minutes to hours timescales (Figure 2, Supplement 1) that would have been resource and time intensive, and likely impossible, to gather via histology alone.
The reviewer appropriately underscores the utility of in vivo imaging above histological-only investigation. In response, we have added text in the introduction to emphasize the nuanced, but important value of both longitudinal imaging as well as dynamic imaging which is not possible with conventional histology (e.g. blood perfusion status, immune cell interactions etc.)
P3-4 L21-42 (these points also addressed in response to reviewer #2 above)
(2) A few questions and comments on the laser ablation model<br /> - It is alluded to in the Discussion in Lines 519-521 that the procedure is highly reproducible (95%) but the associated data for this repeatability metric is not shown.
We agree that the criterion for determining a “successful lesion” requires further elaboration. Therefore, we have now included the criteria for successful lesions in the methods as well as discussion (in bullet below):
Methods:
P9-10 L129-133: “This protocol produced a hyper-reflective phenotype in the >40 locations across 28 mice. In rare cases, the exposure yielded no hyper-reflective lesion and were often in mice with high retinal motion, where the light dosage was spread over a larger retinal area. These locations were not included in the in-vivo or histological analysis.”
- The methods state that a 24 x 1-micron line is focused on the retina, but all lesions seem to appear elliptical where the major to minor axis ratio is a lot smaller than this intended size. One wonders what leads to this discrepancy.
We expect that this observation is related to the response above, we have added the following:
Discussion:
P27 L497-505: “The damage took on an elliptical form, likely due to: 1) Eye motion from respiration and heart rate which spreads the light over a larger integrative area (rather than line). 2) The impact of focal light scatter. 3) A micron-thin line imparting damage on cells that are many microns across manifesting as an ellipse. The majority of light exposures produced lesions of this elliptical shape. In a few conditions, for the reasons described above, the exposure failed to produce a strong, focal damage phenotype. To improve lesion reproducibility, future experiments should control for subtle eye motion affecting light damage, especially for long exposures.”
(3) Lastly, a thickening is noted in the ONL after laser injury that seems to cause a thinning of the INL as well (Figure 3) which may increase the apparent INL nuclei density.
The reviewer’s careful eye finds local swelling after injury. However, despite swelling, the segregation between INL and ONL was maintained in all days we examined. Thus, no ONL cells were included in INL counts (see figure 3A & 3D).
Also, the ONL - inner (panel B) seems to show a little reduction in cell density in the same elliptical shape as the outer ONL in panel C.
We agree with this observation and was one of the reasons we included this detailed analysis of both the inner and outer half of the ONL. Our finding is that there is more prominent loss of nuclei in the outer half of the ONL. While the mechanism for this is not understood, we felt it was an important finding to include and further shows the axial specificity of the light damage we are inducing (especially at day 1 observation).
Lastly, the reduction in nuclear density is visually obvious in the ONL at the 1 and 3-day time points but the p-statistic does not seem to convey this. One may consider performing the analysis on panel F on a smaller region surrounding the lesion to more reliably reveal these effects.
Related to the response above, the ONL shows a persistence of nuclei in the upper half of that layer, whereas the outer half, shows a visible reduction. Therefore, we expect that the reviewer is correct that a statistical analysis that considers just the outer half of the ONL would likely show a strong statistical significance. The challenge, however, is that our analysis strategy counted all cells within a 50 micron diameter cylinder through the entirety of the ONL (meaning strong loss in the outer half was attenuated by weak loss in the inner half). A more detailed sub-layer analysis is challenging given the notable retinal remodeling over days-to-weeks that make it challenging to attribute layers within the ONL as viable landmarks for the requested analysis.
(4) In Figure 6, the NIR confocal image and fluorescent microglia seem to share the same shape, starting from the OPL and posterior to it. This is particularly evident in the 3 and 7-day time points in the ONL and ONL/IS images. This departs from lines 567-577 where the claim is made that the hyperreflective phenotype in NIR images does not emerge from the microglia and neutrophils. This discrepancy should be clarified. It may be so that the hyperreflective phenotype as observed by Figure 2 at shorter timescales is not related to the microglia but the locus of hyper-reflections changes at longer time scales to involve the microglia as well as in Figure 6. One potential clue/speculation of the common shapes/size in confocal hyper-reflectance and fluorescent microglia of Figure 6 comes from Figure 9 where the microglia seem to engulf the photoreceptor phagosomes in the DAPI stains. It is possible that the hyper-reflections arise from the phagosomes but their co-localization with microglia seems to demonstrate a shared size/shape. As an addendum to the first point, such correlations are a power of the in vivo model and impossible to achieve in histology.
The reviewer shows a deep understanding of our data. We agree with many of the points, but for the purpose of the paper many of the above offerings are speculative and we have chosen not to elaborate on these points as it is not definitive from the data. Instead, we direct the reader to an important finding that within hours, the hyper-reflective phenotype is seen in both OCT and AOSLO, whereas microglial somas/processes have not yet migrated into the hyper-reflective region. We have now emphasized this point in the discussion section:
P29-30 L543-552: “A common speculation is that the increased backscatter may arise from local inflammatory cells that activate or move into the damage location. In our data, confocal AOSLO and OCT revealed a hyperreflective band at the OPL and ONL after 488 nm light exposure (Figure 2a, b). We found that the hyperreflective bands appeared within 30 minutes after the laser injury, preceding any detectable microglial migration toward the damage location (Figure 2 – figure supplement 1 and Figure 6 – figure supplement 1). We thus conclude that the initial hyperreflective phenotype is not caused by microglial cell activity or aggregation.”
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Author response:
The following is the authors’ response to the original reviews
Reviewer #1:
To gain further insight into the dynamics of microglial aging in the hippocampus, the authors used a bioinformatics method known as "pseudotime" or "trajectory inference" to understand how cells may progress through different functional states, as defined by cellular transcriptome (15,16). These bioinformatics approaches can reveal key patterns in scRNAseq / snRNAseq datasets and, in the present study, the authors conclude that a "stress response" module characterized by expression of TGFb1 represents a key "checkpoint" in microglial aging in midlife, after which the cells can move along distinct transcriptional trajectories as aging progresses. This is an intriguing possibility. However, pseudotime analyses need to be validated via additional bioinformatics as well as follow-up experiments. Indeed, Heumos et al, in their Nature Genetics "Expert Guidelines" Review, emphasize that "inferred trajectories might not necessarily have biological meaning." They recommend that "when the expected topology is unknown, trajectories and downstream hypotheses should be confirmed by multiple trajectory inference methods using different underlying assumptions."(15) Numerous algorithms are available for trajectory inference (e.g. Monocle, PAGA, Slingshot, RaceID/StemID, among many others) and their performance and suitability depends on the individual dataset and nature of the trajectories that are to be inferred. It is recommended to use dynGuidelines(16) for the selection of optimal pseudotime analysis methods. In the present manuscript, the authors do not provide any justification for their use of Monocle 3 over other trajectory inference approaches, nor do they employ a secondary trajectory inference method to confirm observations made with Monocle 3. Finally, follow-up validation experiments that the authors carry out have their own limitations and caveats (see below). Hence, while the microglial aging trajectories identified by this study are intriguing, they remain hypothetical trajectories that need to be proven with additional follow-up experiments.
We thank the reviewer for their suggestion. We have utilized the dynGuidelines kindly provided by the reviewer to utilize an additional trajectory inference tool to analyze our data. We selected Scorpius based on the structure of our data. The tool has provided additional support that microglia progress from a homeostatic state (Cx3cr1, Mef2c) to the induction of stress genes (Hspa1, Atf3) at an intermediate point during aging progression. Furthermore, we observe a concordant increase in ribosomal protein genes at a time point in the pseudotime analysis immediately prior to activation of inflammation-related genes (Il1b, Cst7). These additional analyses support the main findings of our original pseudotime analysis and have been added to the manuscript as Figure S3C,D. Additionally, in the statistical test that uncovers differentially expressed genes along the pseudotime trajectory in this analyses, we find that Tgfb1 is one of the genes that is differentially expressed with peak expression at an intermediate timepoint along the pseudotime trajectory. Furthermore, we have done some preliminary trajectory analysis with slingshot (Street et al, BMC Genomics, PMID: 29914354) that found a similar trajectory with analogous gene expression patterns and dynamic expression of Tgfb1.
To follow up on the idea that TGFb1 signaling in microglia plays a key role in determining microglial aging trajectories, the authors use RNAscope to show that TGFb1 levels in microglia peak in middle age. They also treat primary LPS-activated microglia with TGFb1 and show that this restores expression of microglial homeostatic gene expression and dampens expression of stress response and, potentially, inflammatory genes. Finally, they utilize transgenic approaches to delete TGFb1 from microglia around 8-10mo of age and scRNAseq to show that homeostatic signatures are lost and inflammatory signatures are gained. Hence, findings in this study support the idea that TGFb1 can strongly regulate microglial phenotype. Loss of TGFb1 signaling to microglia in adulthood has already been shown to cause decreased microglial morphological complexity and upregulation of genes typically associated with microglial responses to CNS insults(17-19). TGFb1 signaling to microglia has also been implicated in microglial responses to disease and manipulations to increase this signaling can improve disease progression in some cases(19). In this light, the findings in the present study are largely confirmatory of previous findings in the literature. They also fall short of unequivocally demonstrating that TGFb1 signaling acts as a "checkpoint" for determining subsequent microglial aging trajectory. To show this clearly, one would need to perturb TGFb1 signaling around 12mo of age and carry out sequencing (bulkRNAseq or scRNAseq) of microglia at 18mo and 24mo. Such experiments could directly demonstrate whether the whole microglial population has been diverted to the TGFb1-low aging trajectory (that progresses through a translational burst state to an inflammation state as proposed). Future development of tools to tag TGFb1 high or low microglia could also enable fate tracing type experiments to directly show whether the TGFb1 state in middle age predicts cell state at later phases of aging.
We apologize for the use of the term “checkpoint” when referring to the role of Tgfb1 in microglial aging. Instead, our model posits that Tgfb1 expression increases in response to the early insults of the aging process in an attempt to return microglia to homeostasis. Therefore, this would predict that increasing TGFB1 levels after an insult would decrease activation and age-related progression of microglia, which we demonstrate in vitro (Figure 3). Alternatively, the loss of TGFB1 should prevent microglia from returning to a homeostatic state after an age-related stressor, and thus increase the number of microglia in activated states. We observe this increase in activated microglia in our middle-aged microglia-specific Tgfb1 knockout mouse model. Furthermore, the haploinsufficiency of Tgfb1 at this age indicates that TGFB1 signaling in microglia is sensitive to relative levels of Tgfb1. The transient increase in Tgfb1 expression further suggests that the threshold for TGFB1 signaling is dynamic. Finally, RNA-Seq analysis of both in vitro TGFB1 supplemented microglia and in vivo Tgfb1 depleted microglia highlight that TGFB1 alters the aging microglia transcriptome. Combined, these results provide evidence that Tgfb1 modulates advancement of microglia through an aging continuum.
The present study would also like to draw links between features of microglial aging in the hippocampus and a decline in hippocampal-dependent cognition during aging. To this end, they carry out behavioral testing in 8-10mo old mice that have undergone microglial-specific TGFb1 deletion and find deficits in novel object recognition and contextual fear conditioning. While this provides compelling evidence that TGFb1 signaling in microglia can impact hippocampus-dependent cognition in midlife, it does not demonstrate that this signaling accelerates or modulates cognitive decline (see below). Age-associated cognitive decline refers to cognitive deficits that emerge as a result of the normative brain aging process (20-21). For a cognitive deficit to be considered age-associated cognitive decline, it must be shown that the cognitive operation under study was intact at some point earlier in the adult lifespan. This requires longitudinal study designs that determine whether a manipulation impacts the relationship between brain status and cognition as animals age (22-24). Alternatively, cross-sectional studies with adequate sample sizes can be used to sample the variability in cognitive outcomes at different points of the adult lifespan (22-24) and show that this is altered by a particular manipulation. For this specific study, one would ideally demonstrate that hippocampal-based learning/memory was intact at some point in the lifespan of mice with microglial TGFb1 KO but that this manipulation accelerated or exacerbated the emergence of deficits in hippocampal-dependent learning/memory during aging. In the absence of these types of data, the authors should tone down their claims that they have identified a cellular and molecular mechanism that contributes to cognitive decline.
We agree with the reviewer that to adequately demonstrate an age-dependent effect of microglia-derived TGFB1 on cognition it is necessary to perturb microglial TGFB1 at young and mature ages and assess the age-dependent effect on cognition. To address this, we have now performed a complementary behavioral study utilizing the Tmem119-CreER mouse model to drive the microglia-specific excision of Tgfb1 in two separate cohorts of mice – one young (2-3 months) and one in mature mice (7-8 months) – followed by cognitive testing. Using the novel object recognition test, we find that young mice of all genotypes (WT, Tgfb1 Het and Tgfb1 cKO ) retain the ability to recognize the novel object (as determined by having a significant preference in exploring the novel object). Alternatively, only the WT mature mice demonstrate a preference for the novel object, while the Tgfb1 Het and Tgfb1 cKO show no preference for the novel object. These behavioral data demonstrate an age-dependent necessity for microglia-specific TGFB1 in in maintain proper hippocampal-dependent memory and is now included in the manuscript as revised Figure 4I-J. We have also included additional behavioral tests (Y-Maze and open field) that did not show any difference between the genotypes as Figure S6D-G. Unfortunately, we were unable to perform the fear conditioning testing, as our apparatus broke during this time. Together, these results reveal that there is an age-dependent necessity for microglia-derived TGFB1 for hippocampal-dependent cognitive function.
A final point of clarification for the reader pertains to the mining of previously generated data sets within this study. The language in the results section, methods, and figure legends causes confusion about which experiments were actually carried out in this study versus previous studies. Some of the language makes it sound as though parabiosis experiments and experiments using mouse models of Alzheimer's Disease were carried out in this study. However, parabiosis and AD mouse model experiments were executed in previous studies (25,26), and in the present study, RNAseq datasets were accessed for targeted data mining. It is fantastic to see further mining of datasets that already exist in the field. However, descriptions in the results and methods sections need to make it crystal clear that this is what was done.
The reviewer makes an excellent point. While we referenced the public dataset in the original manuscript, the citation style of superscripted numbers diminishes our ability to adequately reference the datasets. Therefore, we have added the names of the first authors (Palovics for the parabiosis dataset and Sala Frigerio for the Alzheimer’s Disease dataset) to all the instances in the results and figure legends when we refer to these datasets.
Additional recommendations:
Major comments.
(1) There is some ambiguity surrounding how to interpret the microglial TGFb1 knockout that seems incompatible with viewing this molecule as a "checkpoint" in microglial aging. TGFb1 is believed to be primarily produced by microglia. Secreted TGFb1 is then detected by microglial TGFbR2. Are the microglia that have high levels of TGFb1 in middle age signaling to themselves (autocrine signaling)? Or contributing to a local milieu that impacts multiple neighbor microglia (paracrine signaling)? The authors could presumably look in their own dataset to evaluate microglial capacity to detect TGFb1 via its receptors.
We thank the reviewer for this insightful suggestion. We have undertaken analysis of our dataset to assess whether Tgfb1 acts through autocrine or paracrine signaling. To do so, we reanalyzed our microglia aging scRNA-Seq dataset leveraging the variation in microglia Tgfb1 expression to probe the relative activity of TGFB1. Specifically, we partitioned microglia into quartiles based on their Tgfb1 expression, and subsequently investigated the expression of TGFB signaling effectors and targets. High expression of downstream TGFB signaling pathway components in microglia with high Tgfb1 expression would point to autocrine mechanisms while, alternatively, high expression of downstream TGFB signaling pathway components in microglia with low Tgfb1 expression would point to paracrine mechanisms. We observed highest expression of TGFB signaling pathway components and targets in microglia with the highest expression of Tgfb1. These data suggest that Tgfb1 acts through an autocrine mechanism. These results have been added to our manuscript as Figure S4E-G. Additionally, while our manuscript was under review, a paper by Bedolla et al (Nature Communications 2024; PMID: 38906887) was published that investigated the role of Tgfb1 in adult microglia. This paper utilized orthogonal techniques – sparse microglia-specific Tgfb1 knockout and IHC - to also suggest that microglia utilize autocrine Tgfb1 signaling. Together, these complementary data provide strong evidence that Tgfb1 acts through an autocrine mechanism in adult microglia.
(2) Conclusions of the study rest on the assumption that microglial inflammatory responses are a central driver of cognitive decline. They assume that manipulations that increase microglial progression into an inflammatory state will negatively impact cognitive function. Although there are certainly a lot of data in the field that inflammatory factors can impact synaptic function, additional experiments would be required to unequivocally demonstrate that a "TGFb1 dependent" progression of microglia to an inflammatory state underlies any observed changes in cognition. For example, in the context of microglial TGFb1 deletion, can NSAIDs or blockers of soluble TNFa (e.g. XENP345), or blockers of SPP1, etc. rescue behavior? Can microglial depletion in this context rescue behavior? Assuming behavior was carried out in the same microglial TGFb1 KO mice that were used for microglial scRNAseq, they could also carry out linear regression-type analyses to link microglial inflammatory status to the behavioral performance of individual mice. In the absence of additional evidence of this sort, the authors should tone down claims about mechanistic relationships between microglial state and cognitive performance.
We thank the reviewer for realizing that the link between cognition and inflammation in our paper is speculative. Therefore, we have taken the reviewer’s advice and toned down the claims linking inflammation to cognition in our manuscript. Instead, we connect the disruption in cognition to what is observed in our data, a loss of microglia homeostasis and a shift in the microglia aging trajectories.
Additional Recommendations:
Minor comments:
(1) Ideally at some point in the results or discussion, the authors should acknowledge that the hippocampus has highly distinct sub-regions and that microglia show different functions and properties across these sub-regions (e.g. microglia in hilus and subgranular zone vs microglia in stratum radiatum, vs microglia immediately adjacent to or embedded within stratum pyrimidale). Do expression levels of TGFb1 and microglial aging trajectories vary across sub-regions? To what extent can this account for heterogeneity of aging trajectories observed in microglial aging within the hippocampus?
We are interested in how microglia heterogeneity during aging is influenced by the specific functions, and thus microenvironments within the hippocampus. Therefore, we have expanded our IHC analysis of microglia to determine how the microenvironment influences microglia phenotypes by looking at several different regions of the hippocampus. We have included this regional analysis as Figure S2 in the manuscript. This analysis has revealed region-specific effects on microglia activation during aging.
(2) For immunohistochemistry data, it is not particularly convincing to see one example of one cell from each condition. Generally, an accepted approach in the field is to present lower magnification images accompanied by zoom panels for several cells from each field of view. This reassures the reader that specific cells haven't simply been "cherry-picked" to support a particular conclusion.
To allay the concerns of the reviewer that cells haven’t been “cherry-picked”, we have provided low magnification images for the aging CD68 and NF<sub>κ</sub>B stains in Supplemental Figure S2.
(3) In immunohistochemistry data, have measures been taken to ensure that observed signals are not simply autofluorescence that becomes prominent in tissues with aging? (i.e. use of trueblack or photoquenching of tissue prior to staining) See PMID 37923732
We agree that autofluorescence, at least partially due to the accumulation of lipofuscin, becomes prominent in certain regions and cells of the hippocampus during aging. This most prominently occurs in the microglia of the hilus. This autofluorescence has a particular subcellular distribution, as it is localized to lyso-endosomal bodies. The microglia activation marker CD68 is also localized to lysosomes. A previous publication by Burns et al (eLife; PMID: 32579115) identified autofluorescent microglia (AF+) with unique molecular profiles that accumulate with age. They posited that these AF+ microglia resembled other microglia subsets that have pronounced storage compartments, such as the pro-inflammatory lipid droplet-containing microglia that accumulate with age reported by Marschallinger et al (Nature; PMID: 31959936). As such, autofluorescence present in microglia potentially represents distinctive and functional states of microglia. Our CD68 immunostaining accumulates with age, which could overlap with autofluorescent storage bodies. Thus, we performed a complementary CD68 immunostaining in an independent cohort of young (3 months) and aged (24 months) mice with autofluorescence quencher TrueBlack, and found that the staining pattern and accumulation of CD68 microglia with age persisted as previously observed after use of this quencher (see Authpr response image 1). Images are IBA1 (cyan) and CD68 (yellow) with the molecular layer (ML), granule cell (GC), and hilus illustrated and corresponding quantification provided (Two-way ANOVA with Sidak’s multiple comparisons test; ***P<0.001; ****P<0.0001).
We would like to note that the subcellular localization of the other immunostainings included in the manuscript was distinct from CD68, and not likely to be associated with the autofluorescent storage bodies. Additionally, our RNAScope staining for Tgfb1 did not show an accumulation with age, but rather a transient increase at 12 months of age, which indicates that the interpretation of the RNAScope stain for Tgfb1 was not unduly influenced by autofluorescence.
Author response image 1.
(4) Ideally, more care is needed with the language used to describe microglial state during aging. The terms "dystrophic," "dysfunctional," and "inflammatory" all carry their own implications and assumptions. Many changes exhibited by microglia during aging can initially be adaptive or protective, particularly during middle age. Without additional experiments to show that specific microglial attributes during aging are actively detrimental to the tissue and additional experiments to show that microglia have ceased to be capable of engaging in many of their normal actions to support tissue homeostasis, the authors should exercise caution in using terms like dysfunctional.
We appreciate the reviewers’ suggestion. To allay the concerns of the reviewer about the multiple implications of terms such as “dysfunctional” and “inflammatory”, we have tried to replace them throughout the text with more specific terms.
Reviewer #2:
That said, given what we recently learned about microglia isolation for RNA-seq analysis, there is a danger that some of the observations are a result of not age, but cell stress from sample preparation (enzymatic digestion 10min at 37C; e.g. PMID: 35260865). Changes in cell state distribution along aging were made based on scRNA-seq and were not corroborated by any other method, such as imaging of cluster-specific marker expression in microglia at different ages. This analysis would allow confirming the scRNA-seq data and would also give us an idea of where the subsets are present within the hippocampus, and whether there is any interesting distribution of cell states (e.g. some are present closer to stem cells?). Since TGFb is thought to be crucial to microglia biology, it would be valuable to include more analysis of the mice with microglia-specific Tgfb deletion e.g. what was the efficiency of recombination in microglia? Did their numbers change after induction of Tgfb deletion in Cx3cr1-creERT2::Tgfb-flox mice.
We thank the reviewer for their comment regarding potential ex vivo transcriptional alterations with the approaches used in our study. We performed our aging microglia scRNA-Seq characterization prior to the release of Marsh et al (Nature Neuroscience; PMID: 35260865), which revealed the potential transcriptional artefacts induced by isolation. That being said, we took great care to minimize the amount of time samples were subjected to enzymatic digestion (15 minutes) and kept cells at 4C during the remainder of the isolation. Furthermore, we performed all isolations simultaneously, so that transcriptional changes induced by the isolation would be present across all ages and should not be observed during our analysis unless indicative of a true age-related change. Additionally, we have corroborated changes in cell state distribution across ages using several markers (Tgfb1 and KLF2 for the intermediate stress state, S6 for the translation state, and NFKB and CD68 for activation states). In the revised manuscript, we have added additional hippocampal subregion analysis of several IHC immunostains to provide spatial insights into the microglia aging process (Figure S2). This analysis reveals unique spatial dynamics of microglia aging. For example, as the reviewer foresaw, we found that the granule cell layer (the location of adult hippocampal neurogenesis) had a more pronounced age-associated progression of microglial activation than several other regions. A subset of regions had minimal levels of activation during aging, such as the molecular layer and the stratum radiatum of the CA1 (inner CA1in the manuscript) – regions enriched in synaptic terminals. Furthermore, this analysis highlights the susceptibility of microglia aging to microenvironmental influences.
Regarding the temporally controlled microglia-specific genetic KO mouse model used in our original submission, the Cx3cr1-CreER allele selected (B6.129P2(Cg)-Cx3cr1tm2.1(cre/ERT2)Litt/WganJ) has been reported to have very high recombination efficiency (~94% in Parkhurst et al (Cell; PMID: 24360280)), and we used a tamoxifen induction protocol very similar to Faust et al. (Cell Reports; PMID: 37635351) that achieved ~98% recombination (they injected 100mg/kg for 5 days, while we injected 90mg/kg for 5 days). We analyzed our scRNA-Seq data for the expression of Tgfb1 and found that the knockout mice had a 67% reduction in cells expressing higher levels of Tgfb1 (see panel A in Author response image 2). This is likely a large underestimate of the recombination efficiency, as exon 3 is floxed and residual nonfunctional transcripts could be present, given nonsense-mediated decay is not realized in a number of knockout lines (Lindner et al, Methods, PMID: 33838271). We likely achieved a much higher excision efficiency. We would like to highlight that our data indicating increased microglia activation after tamoxifen treatment (Figure S5A) and the involvement of autonomous signaling (Figure S4E-G) are consistent with recently published work by Bedolla et al, (Nature Communications; PMID: 38906887). Additionally, as part of the revision process, we have now corroborated our behavioral data using and independent temporally controlled microglia-specific KO mouse model - Tmem119-CreER::Tgfb1 knockout mice (Figure 4I-K). We performed qPCR on sorted microglia to determine RNA levels in wildtype and knockout mice. Relative levels of Tgfb1 and exon 3 of Tgfb1 (the floxed exon) on technical replicates of 3 pooled samples indicated overall loss of Tgfb1 expression, as well as undetectable levels of exon 3 as normalized to Actb (see panel B in Author response image 2).
Author response image 2.
With respect to the effects of aging and Tgfb1 on microglia density, we find a slight region-specific increase in microglia density with age (see Author response image 3). The density of Iba1 cells across hippocampal regions was analyzed at 3 and 24 months of age (see panel A in Author response image 3) and along an aging continuum at 3, 6, 12, 18, and 24 months (see panel B in Author response image 3). These data are also included in the revised manuscript (Figure S2D-F).
Author response image 3.
Deletion of Tgfb1 also had region-specific effects on microglia. While there was no difference in microglia density between wildtype and heterozygous microglia, there was a significant increase in microglia density in the hilus and molecular layers in knockout mice (see Author response image 4) and included in the revised manuscript (Figure S5A). These data indicate that there are subtle region-specific increases in microglia density with age, as well as following the deletion of Tgfb1 from microglia of mature mice.
Author response image 4.
Additional Recommendations:
(1) The problem of possible digestion artifacts in scRNA-seq should be at least addressed in the discussion as a caveat in data interpretation. Staining for unique cluster markers in undigested tissue would solve the problem. It can be done with microscopy or using flow cytometry, but for this microglia, isolation should be done with no enzymes or with Actinomycin (PMID: 35260865).
The ex vivo activation signature uncovered by Marsh et al. (Nature Neuroscience; PMID: 35260865) arises from the digestion methods used to isolate microglia. We took the utmost care in processing our microglia identically within experiments, which should minimize the amount of uneven ex vivo activation of microglia. This is borne out by the structures of our single-cell sequencing data. Unlike Marsh et al_. where they observe unique cluster after addition of their inhibitors, we do not see any clusters unique to a single condition, suggesting that any influence of _ex vivo activation was evenly distributed.
Importantly, as suggested by the review, we have we have complemented our scRNA-Seq analysis by corroborating several markers for various stages of microglia aging progression using RNAScope and IHC in intact tissue. Specifically, the transient age-dependent increase in Tgfb1 high microglia was confirmed using RNAScope (Figure 3B), the age-related increase in ribosomal high microglia was confirmed using S6 immunostaining (Figure 3I), and the increase of various markers of age-associated activation (C1q, CD68 and NFkB) was confirmed using immunostaining (Figure 1F and Figure S2D-I). Additionally, we have also performed immunostainings for KLF2 and confirmed peak microglia expression at 18 months of age with lower levels at 24 months of age (Figure 2H).
(2) The figures of GO and violin plots are not easy to follow sometimes... what are the data points in the violin plots, maybe worth showing them as points? For the GO, e.g. in 3D, 3J, including a short description of the figure could help, e.g. in Figure 1. it was clear.
We chose not to include the datapoints in the violin plots for aesthetic purposes. Each violin plot would have had hundreds of points that would have made the plots very busy and hidden the structure of the distribution. In Author response image 5 we show the violin plot in Figure 2M with (panel A) and without (panel B) individual points. In a small format, the points overlap and become jumbled together. Therefore, we chose to present the violin plots without points for clarity on the data structure. As for the gene ontology plots in Figure 3, we have updated the descriptions in both the text and figure legends to provide clarification on what they represent.
Author response image 5.
(3) I'm very curious to see the mechanism of action of "aged" microglia in the TGFb-depletion model. Is it creating hostile conditions for stem cells, or we have increased synapse loss? Something else?
We thank the reviewer for their insightful questions. We would like to note that during the revision process of our manuscript, a complementary study was published reporting that the loss of microglia-derived Tgfb1 leads to an aberrant increase in the density of dendritic spines in the CA1 region of the hippocampus (Bedolla et al, Nature Communications, PMID: 38906887). The data from Bedolla et al, shows sparsely labeled neurons in the CA1 with a mGreenLantern expressing virus in mice the had Tgfb1 deleted from microglia using the Cx3cr1-CreERT driver (Figure 7U,V). Additionally, McNamara et al (Nature; PMID: 36517604) demonstrated that microglia-derived Tgfb1 signaling regulates myelin integrity during development and several studies have revealed links between Tgfb1 signaling and altered neurogenesis (e.g., He et al, Nature, PMID: 24859199 and Dias et al, Neuron, PMID: 25467979). Together, this growing body of work indicates that microglia-derived TGFB1 regulates myelination, neurogenesis and synaptic plasticity, which have all been shown to play a role in cognition.
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
__* SUMMARY
This study utilizes the developing chicken neural tube to assess the regulation of the balance between proliferative and neurogenic divisions in the vertebrate CNS. Using single-cell RNAseq and endogenous protein tagging, the authors identify Cdkn1c as a potential regulator of the transition towards neurogenic divisions. Cdkn1c knockdown and overexpression experiments suggest that low Cdkn1c expression enhances neurogenic divisions. Using a combination of clonal analysis and sequential knockdown, the authors find that Cdkn1c lengthens the G1 phase of the cell cycle via inhibition of cyclinD1. This study represents a significant advance in understanding how cells can transition between proliferative and asymmetric modes of division, the complex and varying roles of cycle regulators, and provides technical advance through innovative combination of existing tools.
MAJOR AND MINOR COMMENTS *__
Overall Sample numbers are missing or unclear throughout for all imaging experiments. The authors should add numbers of cells analysed and/or numbers of embryos for their results to be appropriately convincing.
This information is now provided in the figure legends (numbers of cells analyzed and/or numbers of embryos) except for data in Figure 5, which are presented in a new Supplementary Table
Values and error bars on graphs must be defined throughout. Are the values means and error bars SD or SEM?
We have used SD throughout the study. This information has now been added in figure legends.
Results 2
____A reference should be provided for cell type distribution in spinal neural tube, where the authors state that cell bodies of progenitors reside within the ventricular zone.
We now cite a recent review on spinal cord development (Saade and E. Marti, Nature Reviews Neuroscience, 2025) to illustrate this point
The authors state that Cdkn1c "was expressed at low levels in a salt and pepper fashion in the ventricular zone, where the cell bodies of neural progenitors reside, and markedly increased in a domain immediately adjacent to this zone which is enriched in nascent neurons on their way to the mantle zone. In contrast, the transcript was completely excluded from the mantle zone, where HuC/D positive mature neurons accumulate." It is not clear if this is referring only to E4 or also to E3 embryos. Indeed, Cdkn1c expression appears to be much more salt and pepper at E3 and only resolves into a clear domain of high expression adjacent to the mantle zone at E4. It may be helpful if this expression pattern could be described in a bit more detail highlighting the changes that occur between E3 and E4.
We have now reformulated this paragraph as follows: "At E3, the transcript was expressed at low levels in a salt and pepper fashion in the ventricular zone, where the cell bodies of neural progenitors reside (Saade and Marti, 2025)). One day later, at E4, this salt and pepper expression was still detected in the ventricular zone, while it markedly increased in the region of the mantle zone that is immediately adjacent to the ventricular zone. This region is enriched in nascent neurons on their way to differentiation that are still HuC/D negative. In contrast, the transcript was completely excluded from the more basal region of the mantle zone, where mature HuC/D positive neurons accumulate.
It would be useful to annotate the ISH images in Fig 2A to show the ventricular and mantle zones as defined by immunofluorescence.
Thank you for the suggestion. We have now added a dotted line that separates the ventricular zone from the mantle zone at E3 and E4 in Figure 2A
Reference should be included for pRb expression dynamics.
This section has been rewritten in response to comments from Reviewer #3, and now contains several references regarding pRb expression dynamics. See detailed response to Reviewer #3 for the new version
Could the Myc tag insertion approach disrupt protein function or turnover? ____Why was the insertion target site at the C terminus chosen?
The first reason was practical: at the time when we decided to generate a KI in Cdkn1c, we had already generated several successful KIs at C-termini of other genes, in particular using the P2A-Gal4 approach (see Petit-Vargas et al, 2024), and had not yet experimented with N-terminal Gal4-P2A. We therefore decided to use the same approach for Cdkn1c.
We also chose to target the C-terminus to avoid affecting the active CKI domain which is located at the N-terminus.
Nevertheless, the C-terminal targeting may have an impact on the turnover: it has been described that CDK2 phosphorylation of a Threonin close to the C-terminus of Cdkn1c leads to its targeting for degradation by the proteasome from late G1 (Kamura et al, PNAS, 2003; doi: 10.1073/pnas.1831009100). We can therefore not rule out that the addition of the Myc tags close to this phosphorylation site modulates the dynamics of Cdkn1c degradation. We note, however, that we observed little overlap between the Cdkn1c-Myc and pRb signals in cycling progenitors, suggesting that Cdkn1c is effectively degraded from late G1.
OPTIONAL Could a similar approach be used to tag Cdkn1c with a fluorescent protein to enable live imaging of dynamics?
Although it could be done, we have not attempted to do this for CDKN1c because our current experience of endogenous tagging of several genes with a similar expression level (based on our scRNAseq data) and nuclear localization (Hes5, Pax7) with a fluorescent reporter shows that the fluorescent signal is extremely low or undetectable in live conditions; Therefore we favored the multi-Myc tagging approach, and indeed we find that the Myc signal in progenitors is also very low even though it is amplified by the immunohistology method; this suggests that most likely, the only signal that would be detected -if any- with a fluorescent approach would be the peak of expression in newborn neurons.
In suppl Fig 1C nlsGFP-positive cells are shown in the control shRNA condition. How can this be explained and does it impact the interpretation of the findings?
The reviewer refers to the control gRNA condition in panel C, that shows that two small patches of GFP-positive cells are visible in the whole spinal cord of this particular embryo.
Technically, the origin of these "background" cells could be multiple. A spontaneous legitimate insertion at the CDKN1c locus by homologous recombination is possible, although we tend to think it is unlikely, given the extremely short length of the arms of homology; illegitimate insertions of the Myc-P2A-Gal4 cassette at off-target sites of the control gRNA is a possibility. Alternatively, a low-level leakage of Gal4 expression from the donor vector could lead to a detectable nls-GFP expression in a few cells via Gal4-UAS amplification.
In any case, these cells are observed at a very low frequency (1 or 2 patches of cells/embryo) relative to the signal obtained in presence of the CDKN1c gRNA#1 (probably several thousand positive cells per embryo). This suggests that if similar "background" cells are also present in presence of the CDKN1c gRNA, they would not significantly contribute to the signal, and would not impact the interpretation.
In Fig 2B, there are a number of Myc labelled cells in the mantle zone, whereas the in situ images show no appreciable transcript expression. Is this because the protein but not the transcript is present in these cells? Could the authors comment on this?
It is indeed possible that the CDKN1c protein is more stable than the transcript in newborn neurons and remains detectable in the mantle zone after the mRNA disappears. In Gui et al, 2006, where they use an anti-CDKN1c antibody to label the protein in mouse spinal cord transverse sections at E11.5 (Figure 1B), a few positive cells are also visible basally. They could correspond to neurons that have not yet degraded CDKN1c, although it is unclear in the picture whether these cells are really in the mantle zone or in the adjacent dorsal root ganglion; we note that a similar differential expression dynamics between mRNA and protein has been described for Tis21/Btg2 in the developing mouse cortex, where the protein, but not the mRNA, is detected in some differentiated bIII-tubulin-positive neurons (Iacopetti et al, 1999).
However, related to our response above to a previous comment from the same reviewer, we cannot rule out the possibility that the Myc tags modulate the turnover of CDKN1c protein and slow down the dynamics of its degradation in differentiating neurons.
We have added a sentence to indicate the presence of these cells: "In addition, a few Myc-positive cells were located deeper in the mantle zone, where the transcript is no more present, suggesting that the protein is more stable than the transcript."
Results
It should be mentioned how mRNA expression levels were quantified in the shRNA validation experiment (supp Fig 2A).
We did not quantify the level of mRNA reduction, it was just evaluated by eye. The reason for choosing shRNA1 for the whole study was dictated by 1) the fact that we more consistently saw (by eye) a reduction in the signal on the electroporated side with this construct than with the other shRNAs, and 2) that the effect on neurogenesis was also more consistent.
We will perform additional experiments to provide some quantitation of the shRNA effect, as this is also requested by Reviewer #3.
As our Cdkn1c KI approach offers a direct read-out of the protein levels in the ventricular and mantle zones, and since our shRNA strategy of "partial knock-down" is based on the idea that the shRNA effect should be more complete in progenitors expressing Cdkn1c at low levels than in newborn progenitors that express the protein at a higher level, we propose to validate the shRNA in the Cdkn1c-Myc knock-in background, by comparing the Myc signal intensity between control and Cdkn1c shRNA conditions
Figure panels are not currently cited in order. Citation or figure order could be changed.
We have now added a common citation of the panels referring to analyses at 24 and 48 hours after electroporation (now Figure 3A-F), allowing us to display the experimental data on the figure according to the timing post electroporation, while the text details the phenotype at the later time point first.
The authors should provide representative images for the graphs shown in Fig 3A and 3B. These could go into supplementary if the authors prefer.
We have added images in a revised version of the Figure 3, as requested
A supplementary figure showing the Caspase3 experiment should be added.
We have added data showing Caspase3 experiments in Supplementary Figure 3D
OPTIONAL. Identification of sister cells in the clonal analysis experiments is based on static images and cannot be guaranteed. Could live imaging be used to watch divisions followed by fixation and immunostaining to confirm identity?
We agree with the reviewer that direct tracking is the most direct method for the identification of pairs of sister cells. However, it remains technically challenging, and the added value compared to the retrospective identification would be limited, while requiring a great workload, especially considering the many different experimental conditions that we have explored in this study.
Results 4
How did the authors quantify the intensity of endogenous Myc-tagged Cdkn1c to confirm the validity of the Pax7 locus knock in? Can they show that the expression level was consistently lower than the endogenous expression in neurons? Quantification and sample numbers should be shown.
We have not done these quantifications in the original version of the study. We will add a quantification of the signal intensity in the ventricular and mantle zones for the revised version of the manuscript, as also requested by reviewer #3.
In Fig 4B, the brightness of row 2 column 1 is lower than the same image in row 2 column 2, which is slightly misleading, since it makes the misexpressed expression level look lower than it is compared with endogenous in column 3. Is this because only a single z-section is being displayed in the zoomed in image? If so, this should be stated in the figure legend.
All images in the figure are single Z confocal images. Images in Column 2 (showing both electroporated sides of the same tube) were acquired with a 20x objective, whereas the insets shown in Columns 1 and 3 are 100x confocal images. 100x images on both sides were acquired with the same acquisition parameters, and the display parameters are the same for both images in the figure. The signal intensity can therefore be compared directly between columns 1 and 3.
We have modified the legend of the Figure to indicate these points: "The insets shown in Columns 1 and 3 are 100x confocal images acquired in the same section and are presented with the same display parameters".
In Fig 4D, the increase in neurogenic divisions is mainly because of the rise in terminal NN divisions according to the graph, but no clear increase in PN divisions. Could the authors comment on the significance of this?
Our interpretation is that Pax7-CDKN1c misexpression experiments cause both PP to PN and PN to NN conversions. This is coherent with the classical idea of a progressive transition between these three modes of division in the spinal cord. Coincidentally, in our experimental conditions (timing of analysis and level of overexpression), the increase in PN resulting from PP to PN conversions is perfectly balanced by a decrease resulting from PN to NN conversions, giving the artificial impression that the PN compartment is unaffected. A less likely hypothesis would be that misexpression directly transforms symmetric PP into symmetric NN divisions, and that asymmetric PN divisions are insensitive to CDKN1c levels. We do not favor this hypothesis, because one would expect, in that case, that the shRNA approach would also not affect the PN compartment, and it is not what we have observed (see Figure 3H - previously 3F).
We have modified the manuscript to elaborate on our interpretation of this result: "We observed an increase in the proportion of terminal neurogenic (NN) divisions and a decrease in proliferative (PP) divisions (Figure 4D). This suggests that CDKN1c premature expression in PP progenitors converts them to the PN mode of division, while the combined endogenous and Pax7-driven expression of CDKN1c converts PN progenitors to the NN mode of division. Coincidentally, at the stage analyzed, PP to PN conversions are balanced by PN to NN conversions, leaving the PN proportion artificially unchanged. The alternative interpretation of a direct conversion of symmetric PP into symmetric NN divisions is less likely, because the PN compartment was affected in the reciprocal CDKN1c shRNA approach (see Figure 3H)."
Results 5 ____The proportion of pRb-positive progenitors having entered S phase was stated to be higher at all time points; however, it is not significantly higher until 6h30 and is actually trending lower at 2h30.
Thank you for pointing this out. We have modified the sentence in the main text.
"We found that the proportion of pRb positive progenitors having entered S phase (EdU positive cells) was significantly higher at all time points examined more than 4h30 after FT injection in the Cdkn1c knock-down condition compared to the control population (Figure 5D)"
OPTIONAL Could CyclinD1 activity be directly assessed?
This is an interesting suggestion. For example, using the fluorescent CDK4/6 sensor developed by Yang et al (eLife, 2020; https://doi.org/10.7554/eLife.44571) in a CDKN1c shRNA condition would represent an elegant experimental alternative to complement our rescue experiments with the double CDKN1c/CyclinD1 shRNA. However, we fear that setting up and calibrating such a tool for in vivo usage in the chick embryo represents too much of a challenge for incorporation in this study.
General ____Scale bars missing fig s1c s4d.
Thanks for pointing this out. Scale bars have been added in the figures and corresponding legends
OPTIONAL Some of the main findings be replicated in another species, for example, mouse or human to examine whether the mechanism is conserved.
OPTIONAL Could use approaches other than image analysis be used to reinforce findings, for example biochemical methods, RNAseq or FACS?
We agree that it will be interesting and important that our findings are replicated in other species, experimental systems, and even tissues, or by alternative experimental approaches. Nevertheless, it is probably beyond the scope of this study.
A model cartoon to summarise outcomes would be useful.
We thank the reviewer for the suggestion. We will propose a summary cartoon for the revised version of the manuscript.
Unclear how cells were determined to be positive or negative for a label. Was this decided by eye? If so, how did the authors ensure that this was unbiased?
Positivity or negativity was decided by eye. However, for each experiment, we ensured that all images of perturbed conditions and the relevant controls were analyzed with the same display parameters and by the same experimenter to guarantee that the criteria to determine positivity or negativity were constant.
Reviewer #1 (Significance (Required)):
SIGNIFICANCE
Strengths: This manuscript investigates the mechanisms regulating the switch from symmetric proliferative divisions to neurogenic division during vertebrate neuronal differentiation. This is a question of fundamental importance, the answer to which has eluded us so far. As such, the findings presented here are of significant value to the neurogenesis community and will be of broad interest to those interested in cell divisions and asymmetric cell fate acquisition. Specific strengths include:
- Variety of approaches used to manipulate and observe individual cell behaviour within a physiological context.
- A limitation of using the chicken embryo is the lack of available antibodies for immunostaining. The authors take advantage of recent advances in chicken embryo CRISPR strategy to endogenously tag the target protein with Myc, to facilitate immunostaining.
- Innovative combination of genetic and labelling tools to target cells, for example, use of FlashTag and EdU in combination to more accurately assess G1 length than the more commonly used method.
- Premature misexpression demonstrates that the previously observed dynamics indeed regulate cell fate.
- Mechanistic insight by examining downstream target CyclinD1.
- Clearly presented with useful illustrations throughout.
- Logic is clear and examination thorough.
- Conclusions are warranted on the basis of their findings. ____Limitations ____T____his study primarily used visual analysis of fixed tissue images to assess the main outcomes. To reinforce the conclusions, these could be supplemented with live imaging to appreciate dynamics, or biochemical techniques to look at protein expression levels.
Some aspects of quantification require explanation in order for the experiments to be replicated.
It is imperative that precise sample sizes are included for all experiments presented.
Advance: ____First functional demonstration role for Cdkn1c in regulating neurogenic transition in progenitors.
Conceptual advance suggesting Cdkn1c has dual roles in driving neurogenesis: promoting neurogenic divisions of progenitors and the established role of mediating cell cycle exit previously reported.
Technical advances in the form of G1 signposting and endogenous Myc tagging using CRISPR in chicken embryonic tissue.
Audience:
Of broad interest to developmental biologists. Could be relevant to cancer, since Cdkn1c is implicated.
Please define your field of expertise with a few keywords to help the authors contextualize your point
Developmental biology, vertebrate embryonic development, neuronal differentiation, imaging. Please note that we have not commented on RNAseq experiments as these are outside of our area of expertise.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
The work by Mida and colleagues addresses important questions about neurogenesis in the embryo, using the chicken neural tube as their model system. The authors investigate the mechanisms involved in the transition from stem cell self-renewal to neurogenic progenitor divisions, using a combination of single cell, gene functional and tracing studies.
The authors generated a new single cell data set from the embryonic chicken spinal cord and identify a transitory cell population undergoing neuronal differentiation, which expresses Tis21, Neurog2 and Cdkn1c amongst other genes. They then study the role of Cdkn1c and investigate the hypothesis that it plays a dual role in spinal cord neurogenesis: low levels favour transition from proliferative to neurogenic divisions and high levels drive cell cycle exit and neuronal differentiation.
Major comments
I have only a general comment related to the main point of the paper. The authors claim that Cdkn1c onset in cycling progenitor drives transition towards neurogenic modes of division, which is different from its role in cell cycle exit and differentiation. Figures 3F and 4D are key figures where the authors analysed PP, PN and NN mode of divisions via flash tag followed by analysis of sister cell fate. If their assumption is correct, shouldn't they also see, for example in Fig. 4D, an increase in PN or is this too transient to be observed or is it bypassed?
As already stated in our response to a similar question from reviewer #1, our interpretation is that Pax7-CDKN1c misexpression experiments cause both PP to PN and PN to NN conversions. This is coherent with the classical idea of a progressive transition between these three modes of division in the spinal cord. Coincidentally, in our experimental conditions (timing of analysis and level of overexpression), the increase in PN resulting from PP to PN conversions is perfectly balanced by a decrease resulting from PN to NN conversions, giving the artificial impression that the PN compartment is unaffected. A less likely hypothesis would be that misexpression directly transforms symmetric PP into symmetric NN divisions, and that asymmetric PN divisions are insensitive to CDKN1c levels. We do not favor this hypothesis, because one would expect, in that case, that the shRNA approach would also not affect the PN compartment, and it is not what we have observed (see Figure 3H - previously 3F).
At the moment, the calculations of PN and NN frequencies are merged in the text, so perhaps describing PN and NN numbers separately will help better understand the dynamics of this gradual process (especially since there is little to no difference in PN).
Regarding the results of Pax7 overexpression presented in figure 4D (now Figure 4E in the revised version), we had made the choice to merge PN and NN values in the main text to focus on the neurogenic transition from PP to PN/NN collectively. We agree with this reviewer, as well as with reviewer #1, that it should be more detailed and better discussed. We therefore propose to modify the paragraph as follows (and as already indicated above in the response to reviewer #1):
"We observed an increase in the proportion of terminal neurogenic (NN) divisions and a decrease in proliferative (PP) divisions (Figure 4D). This suggests that Cdkn1c premature expression in PP progenitors converts them to the PN mode of division, while the combined endogenous and Pax7-driven expression of Cdkn1c converts PN progenitors to the NN mode of division. Coincidentally, at the stage analyzed, PP to PN conversions are balanced by PN to NN conversions, leaving the PN proportion artificially unchanged. The alternative interpretation of a direct conversion of symmetric PP into symmetric NN divisions is less likely, because the PN compartment was affected in the reciprocal Cdkn1c shRNA approach (see Figure 3F, now 3H)."
Could the increase in NN be compatible also with a role in cell cycle exit and differentiation, for example from cells that have been targeted and are still undergoing the last division (hence marked by flash tag) or there won't be any GFP cells marked by flash tag a day after expression of high levels of Cdkn1c?
It is likely that a proportion of cells that would normally have done a NN division are pushed to a direct differentiation that bypasses their last division in the Pax7-CDKN1c condition, and that they contribute to the general increase in neuron production observed in our quantification 48hae (Figure 3F -previously 3C). However, these cases would not contribute to the increase in the NN quantification in pairs of sister cells 6 hours after division at 24hae (Figure 4E - previously 4D), because by design they would not incorporate FlashTag. The rise in NN is therefore the result of a PN to NN conversion.
Basically, what would the effect of expressing higher levels of Cdkn1c be? I guess this will really help them distinguish between transition to neurogenic division rather than neuronal differentiation. If not experimentally, any further comments on this would be appreciated.
These experiments have been performed and presented in the study by Gui et al., 2007, which we cite in the paper. Using a strong overexpression of CDKN1c from the CAGGS promoter, they showed a massive decrease in proliferation, assessed by BrdU incorporation, 24hours after electroporation. We will cite this result more explicitly in the main text, and better explain the difference of our approach. We propose the following modification
« We next explored whether low Cdkn1c activity is sufficient to induce the transition to neurogenic modes of division. A previous study has shown that overexpression of Cdkn1c driven by the strong CAGGS promoter triggers cell cycle exit of chick spinal cord progenitors, revealed by a drastic loss of BrdU incorporation 1 day after electroporation (Gui et al., 2007). As this precludes the exploration of our hypothesis, we developed an alternative approach designed to prematurely induce a pulse of Cdkn1c in progenitors, with the aim to emulate in proliferative progenitors the modest level of expression observed in neurogenic progenitors. We took advantage of the Pax7 locus, which is expressed in progenitors in the dorsal domain at a level similar to that observed for Cdkn1c in neurogenic precursors (Supplementary Figure 6A)."
* * Minor comments
Fig 3C my understanding is that HuC/D should be nuclear, but in fig 3C it seems more cytoplasmic (any comment?)
Some studies suggest that HuC/D can, under certain conditions, be observed in the nucleus of neurons. However, HuC/D is a RNA binding protein whose localization is mainly expected to be cytoplasmic. In our experience (Tozer et al, 2017), and in other publications using the antibody in the chick spinal cord (see, for example, le Dreau et al, 2014), it is observed in the cell body of differentiated neurons, as in the current manuscript.
Fig Suppl 3E (and related 4B), immuno for Cdkn1c-Myc: to help the reader understand the difference between the immuno signals when looking at the figure, I would suggest writing on the panel i) Pax7-Cdkn1c-Myc and ii) endogenous Cdkn1c-Myc, rather than 'misexpressed' and 'endogenous', which is slightly confusing (especially because what it is called endogenous expression is higher).
This has now been modified in the figures.
Literature citing: Introduction and discussion are very nicely written, although they could benefit from some more recent literature on the topic. For example, Cdkn1c role as a gatekeeper of stem cell reserve in the stomach, gut, (Lee et al, CellStemCell 2022 PMID: 35523142) or some other work on symmetric/asymmetric divisions and clonal analysis in zebrafish (Hevia et al, CellRep 2022 PMID: 35675784, Alexandre et al, NatNeur PMID: 20453852), mammals (Royal et al, Elife 2023 37882444, Appiah et al, EMBO rep 2023 PMID: 37382163). Also, similar work has been performed in the developing pancreatic epithelium, where mild expression of Cdkn1a under Sox9rtTa control was used to lengthen G1 without overt cell cycle exit and this resulted in Neurog3 stabilization and priming for endocrine differentiation (Krentz et al, DevCell 2017 PMID: 28441528), so similar mechanisms might be in in place to gradually shift progenitor towards stable decision to differentiate. Moreover, in the discussion, alongside Neurog2 control of Cdkn1c, it could be mentioned that the feedback loop between Cdk inhibitors and neurogenic factor is usually established via Cdk inhibitor-mediated inhibition of proneural bHLHs phosphorylation by CDKs (Krentz et al, DevCell 2017 PMID: 28441528, Ali et al, 24821983, Azzarelli et al 2017 - PMID: 28457793; 2024 - PMID:39575884). Further, in the discussion, could they mention anything about the following open questions: is there evidence for Cdkn1c low/high expression in mammalian spinal cord? Or maybe of other Cdk inhibitors? Is Cdkn1c also involved in cell cycle exit during gliogenesis? Or is there another Cdk inhibitor expressed at later developmental stages, hence linking this with specific cell fate decisions?
We will modify the introduction and discussion in several instances, in order to address the above suggestions and we will:
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add references to its role in other contexts and/or species.
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expand the discussion on the cross talk between neurogenic factors and CDK inhibitors in other cellular contexts.
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add a dedicated paragraph in the discussion to answer reviewer#2's questions: is there evidence for Cdkn1c low/high expression in mammalian spinal cord? Or maybe of other Cdk inhibitors? Is Cdkn1c also involved in cell cycle exit during gliogenesis or is there another Cdk inhibitor expressed at later developmental stages?
Reviewer #2 (Significance (Required)):
The work here presented has important implications on neural development and its disorders. The authors used the most advanced technologies to perform gene functional studies, such as CRISPR-HDR insertion of Myc-tag to follow endogenous expression, or expression under endogenous Pax7 promoter, often followed by flash tag experiments to trace sister cell fate, and all of this in an in vivo system. They then tested cell cycle parameters, clonal behaviour and modes of cell division in a very accurate way. Overall data are convincing and beautifully presented. The limitation is potentially in the resolution between the events of switching to neurogenic division versus neuronal differentiation, which might just warrant further discussion. This work advances our knowledge on vertebrate neurogenesis, by investigating a key player in proliferation and differentiation.
____I believe this work will be of general interest to developmental and cellular biologists in different fields. Because it addresses fundamental questions about the coordination between cell cycle and differentiation and fate decision making, some basic concepts can be translated to other tissues and other species, thus increasing the potential interested audience.
My work focuses on stem cell fate decisions in mammalian systems, and I am familiar with the molecular underpinnings of the work here presented. However, I am not an expert in the chicken spinal cord as a model and yet the manuscript was interesting. I am also not sufficiently expert in the bioinformatic analysis, so cannot comment on the technical aspects of Figure 1 and the way they decided to annotate their data.
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Reviewer #3 (Evidence, reproducibility and clarity (Required)): *__
Summary: In this study, Mida et al. analyze large-scale single-cell RNA-seq data from the chick embryonic neural tube and identify Cdkn1c as a key molecular regulator of the transition from proliferative to neurogenic cell divisions, marking the onset of neurogenesis in the developing CNS. To confirm this hypothesis, they employed classical techniques, including the quantification of neural cell-specific markers combined with the flashTAG label, to track and isolate isochronic cohorts of newborn cells in different division modes. Their findings reveal that Cdkn1c expression begins at low levels in neurogenic progenitors and becomes highly expressed in nascent neurons. Using a classical knockdown strategy based on short hairpin RNA (shRNA) interference, they demonstrate that Cdkn1c suppression promotes proliferative divisions, reducing neuron formation. Conversely, novel genetic manipulation techniques inducing low-level CDKN1c misexpression drive progenitors into neurogenic divisions prematurely.
By employing cumulative EdU incorporation assays and shRNA-based loss-of-function approaches, Mida et al. further show that Cdkn1c extends the G1 phase by inhibiting cyclin D, ultimately concluding that Cdkn1c plays a dual role: first facilitating the transition of progenitors into neurogenic divisions at low expression levels, and later promoting cell cycle exit to ensure proper neural development.
This study presents several ambiguities and lacks precision in its analytical methodologies and quantification approaches, which contribute to confusion and potential bias. To enhance the reliability of the conclusions, a more rigorous validation of the methods employed is essential.
This study introduces a novel approach to tracking the fate of sister cells from neural progenitor divisions to infer the division modes. While previous methods for analyzing the division mode of neural progenitor cells have been implemented, rigorous validation of the approach introduced by Mida et al. is necessary. Furthermore, the concept of cell cycle regulators interacting to control the duration of specific cell cycle stages and influencing progenitor cell division modes has been explored before, potentially limiting the novelty of these findings.
Major comments:
1.-The study presents ambiguity and lacks precision in quantifying neural precursor division modes. The authors use phosphorylated retinoblastoma protein (pRb) as a marker for neurogenic progenitors, claiming its reliability in identifying neurogenic divisions.
However, they do not provide a thorough characterization of pRb expression in the developing chick neural tube, leaving its suitability as a neurogenic division marker unverified.
Throughout their comments on the manuscript, this reviewer raises several points regarding the characterization of pRb expression in our model and of our use of this marker in our study. We take these comments into account and propose to expand on pRb characteristics in the first occurrence of pRb as a marker of cycling cells in the manuscript. The modifications rely on:
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the quotation of several studies showing that phosphorylation of Rb is regulated during the cell cycle, and that "it is not detectable during a period of variable length in early G1 in several cell types (Moser et al, 2018;Spencer et al, 2013; Gookin et al, 2017), including neural progenitors in the developing chick spinal cord (Molina et al, 2022). Apart from this absence in early G1, pRb is detected throughout the rest of the cell cycle until mitosis".
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a more detailed description of our own characterization of pRb dynamics in a synchronous cohort of cycling cells, which reveals a similar heterogeneity in the timing of the onset of Rb phosphorylation after mitosis. This description was initially shown in supplementary figure 3 and will be transferred to a new supplementary figure 2 to account for the fact that it will now be cited earlier in the manuscript.
Regarding the specific question the "suitability (of pRb) as a neurogenic division marker": we do not directly "use phosphorylated retinoblastoma protein (pRb) as a marker for neurogenic progenitors", but we use Rb phosphorylation to discriminate between progenitors (pRb+) and neurons (pRb-) identity in pairs of sister cells to retrospectively identify the mode of division of their mother.
Given that Rb is unphosphorylated during a period of variable length after mitosis (see references above), pRb is not a reliable marker of ALL cycling progenitors. We developed an assay to identify the timepoint (the maximal length of this "pRb-negative" phase) after which Rb is phosphorylated in all cycling progenitors (new Supplementary Figure 2). This assay relies on a time course of pRb detection in cohorts of FlashTag-positive pairs of sister cells born at E3. This time course experiment allowed us to identify a plateau after which the proportion of pRb-positive cells in the cohort remains constant. From this timepoint, this proportion corresponds to the proportion of cycling cells in the cohort. Rb phosphorylation therefore becomes a discriminating factor between cycling progenitors (pRb+) and non-cycling neurons (pRb-).
We are confident that this provides a solid foundation for the determination of the identity of pairs of sister cells in all our Flash-Tag based assays, which retrospectively identify the mode of division of a progenitor on the basis of the phosphorylation status of its daughter cells 6 hours after division.
We propose to modify the main text to describe the strategy and protocol more explicitly, by introducing the sentence highlighted in yellow in the following paragraph where the paired-cell analysis is first introduced (in the section on CDKN1c knock-down):
"This approach allows to retrospectively deduce the mode of division used by the mother progenitor cell. We injected the cell permeant dye "FlashTag" (FT) at E3 to specifically label a cohort of progenitors that undergoes mitosis synchronously (Baek et al., 2018; Telley et al., 2016 and see Methods), and let them develop for 6 hours before analyzing the fate of their progeny using pRb immunoreactivity (Figure 3D). Our characterization of pRb immunoreactivity in the tissue had established beforehand that 6 hours after mitosis, all progenitors can reliably be detected with this marker (Supplementary Figure 2, Methods). Therefore, at this timepoint after FT injection, two-cell clones selected on the basis of FT incorporation can be categorized as PP, PN, or NN based on pRb positivity (P) or not (N) (see Methods, new Figure 3G and new Supplementary Figures 2 and 4)."
We also modified accordingly the legend to Supplementary Figure 2 (previously Supplementary Figure 3, which describes the identification of the plateau of pRb.
Furthermore, retinoblastoma protein (Rb) and cyclin D interact crucially to regulate the G1/S phase transition of the cell cycle, with cyclin D/CDK complexes phosphorylating Rb. Since the authors conclude that CDKN1c primarily acts by inhibiting the cyclin D/CDK6 complex, it is likely that CDKN1c influences pRb expression or phosphorylation state. This raises the possibility that pRb could be a direct target of CDKN1c, whose expression and phosphorylation would be altered in gain-of-function (GOF) and loss-of-function (LOF) analyses of CDKN1c.
In light of this, it would be more appropriate to consider pRb as a CDKN1c target and discuss the molecular mechanisms regulating cell cycle components.
We agree with the reviewer that Rb phosphorylation may be a direct or indirect target of Cdkn1c activity, and exploring the molecular aspects of the cellular and developmental phenomena that we describe in our manuscript would represent an interesting follow up study.
____A more precise approach would involve using other markers or targets to quantify neural precursor division modes at earlier stages of neurogenesis.
To complement our analyses of the modes of division, we propose to use a positive marker to assess neural identity in parallel to the absence of pRb within pairs of cells. This approach may be the most meaningful in the gain of function context (Pax7 driven expression of Cdkn1c) because in this context, the time-point to reach the plateau of Rb phosphorylation used in our FT-based assay may indeed be delayed. On the opposite, in the context of loss of functions, the plateau may be reached earlier, which would have no effect on this assay.
2.-Furthermore, the study employs FlashTag labeling to track daughter cells post-division, but the 16-hour post-injection window may result in misidentification of sister cells due to the potential presence of FlashTagged cells that did not originate from the same division.
This introduces a risk of bias in quantification, data misinterpretation, and potential errors in defining division modes. A more rigorous validation of the FlashTag strategy and its specificity in tracking division pairs is necessary to ensure the reliability of their conclusions.
The reviewer probably mistyped and meant 6-hour post injection, which is the duration that we use for paired cell tracking. We would like to emphasize that in addition to the FlashTag label, we benefit from the electroporation reporter to assess clonality. Altogether, we combine 5 criteria to define a clonal relationship :
- 2 cells are positive for Flash Tag
- The Flash Tag intensity is similar between the 2 cells
- The 2 cells are positive for the electroporation reporter
- The electroporation reporter intensity is similar between the two cells
- the position of the two cells is consistent with the radial organization of clones in this tissue (Leber and Sanes, 1995;__; __Loulier et al, 2014): they are found on a shared line along the apico-basal axis, and share the same Dorso-Ventral and Antero-Posterior position . This combination is already described in the Methods section. We propose to modify the paragraph to include the sentence highlighted in yellow in the text below;
"Cell identity of transfected GFP positive cells was determined as follows: cells positive for pRb and FT were classified as progenitors and cells positive for FT and negative for pRb as neurons. In addition, a similar intensity of both the GFP and FT signals within pairs of cells, and a relative position of the two cells consistent with the radial organization of clones in this tissue (Leber and Sanes, 1995; Loulier et al, 2014) were used as criteria to further ascertain sisterhood. This combination restricts the density of events fulfilling all these independent criteria, and can confidently be used to ensure a robust identification of pairs of sister cells."
3.- The knock-in strategy used to tag the endogenous CDKN1c protein in Figure 2 is an elegant tool to infer protein dynamics in vivo. However, since strong conclusions regarding CDKN1c dynamics during the cell cycle are drawn from this section, it would be advisable to strengthen the results by including quantification with adequate replication and proper statistical analysis, as the current findings are preliminary and somewhat speculative.
- "Although pRb is specific for cycling cells, it is only detected once cells have passed the point of restriction during the G1 phase." Please provide literary reference confirming this observation.
We have entirely remodeled this section, which describes the expression of Myc-tagged Cdkn1c relative to pRb and now provide several references that describe the generally accepted view that pRb is specific of cycling cells, regulated during the cell cycle, and in particular absent in early G1. We also remove the mention of the "Restriction point" in the main text to avoid any confusion on the timing of phosphorylation, as the notion of restriction point is not useful in our study. The section now reads as follows:
"To ascertain that Cdkn1c is translated in neural progenitors, we used an anti-pRb antibody, recognizing a phosphorylated form of the Retinoblastoma (Rb) protein that is specifically detected in cycling cells (Gookin et al., 2017; Moser et al., 2018; Spencer et al., 2013) , including neural progenitors of the developing chick spinal cord (Molina et al., 2022). In the ventricular zone of transverse sections at E4 (48hae), we detected triple Cdkn1c-Myc/GFP/pRb positive cells (arrowheads in Figure 2B), providing direct evidence for the Cdkn1c protein in cycling progenitors. We also observed many double GFP/pRb positive cells that were Myc negative (arrowheads in Figure 2B). The observation of UAS-driven GFP in these pRb-positive cells is evidence for the translation of Gal4 and therefore provides a complementary demonstration that the Cdkn1c *transcript is translated in progenitors. The absence of Myc detection in these double GFP/pRb positive cells also suggests that Cdkn1c/Cdkn1c-Myc stability is regulated during the cell cycle. *
Finally, we observed double Myc/GFP-positive cells that were pRb-negative (Figure 2B; asterisks). One characteristic of Rb phosphorylation as a marker of cycling cells is a period in early G1 during which it is not detectable, as described in several cell types (Gookin et al., 2017; Moser et al., 2018; Spencer et al., 2013) including chick spinal cord neural progenitors (Molina et al., 2022). Using a method that specifically labels a synchronous cohort of dividing cells in the neural tube, we similarly observed a period in early G1 during which pRb is not detectable in some progenitors at E3 (See Supplementary Figure 2 and Methods). Hence, the double Myc/GFP positive and pRb negative cells may correspond to progenitors in early G1. Alternatively, they may be nascent neurons whose cell body has not yet translocated basally (see Figure 2C). Finally, we observed a pool of GFP positive/pRb negative nuclei with a strong Myc signal in the region of the mantle zone that is in direct contact with the ventricular zone (VZ), corresponding to the region where the transcript is most strongly detected (see Figure 2A). This pool of cells with a high Cdkn1c expression likely corresponds to immature neurons exiting the cell cycle and on their way to differentiation (Figure 2B; double asterisks). In addition, a few Myc positive cells were located deeper in the mantle zone, where the transcript is no more present, suggesting that the protein is more stable than the transcript.
In summary, our dual Myc and Gal4 knock-in strategy which reveals the history of Cdkn1c transcription and translation confirms that Cdkn1c is expressed at low level in a subset of progenitors in the chick spinal neural tube, as previously suggested (Gui et al., 2007; Mairet-Coello et al., 2012). In addition, the restricted overlap of Cdkn1c-Myc detection with Rb phosphorylation suggests that in progenitors, Cdkn1c is degraded during or after G1 completion. "
This section will again be remodeled in a future revised version of the manuscript, in which we will add quantifications of Myc levels, as requested by Reviewer 1 above, and also by Reviewer #3 below.
Given that pRb immunoreactivity is used as a marker for cycling progenitors to base many of the results of this study, it would be very valuable to characterize the dynamics of pRb in cycling cells in the studied tissue, for instance combined with the cell cycle reporter used by Molina et al. (Development 2022).
In the original version of the manuscript, the section describing the dynamics of CDKN1c-Myc in the KI experiments presented in Figure 2 relied on the idea that the dynamics of pRb in chick spinal progenitors is similar to what I described in other tissues and cell types, without providing any references to substantiate this fact. Actually, Molina et al provide a characterization of pRb in combination with their cell cycle reporter and conclude that pRb negative progenitors are in G1 ("We also verified that phospho-Rb- and HuC/D-negative cells were in G1 by using our FUCCI G1 and PCNA reporters"). We will now cite this reference to support our claim. In addition, our characterization of Rb progressive phosphorylation in the synchronic Flash-Tag cohort of newborn sister cells provides a complementary demonstration that a fraction of the progenitors are pRb-negative when they exit mitosis (i.e. in early G1). This analysis was initially only introduced in the supplementary Figure 3, as support for the section that presents the Paired-cell assay used in Figure 3. We propose to introduce the data from Supplementary Figure 3 earlier in the manuscript (now Supplementary Figure 2), in order to better introduce the reader with the dynamics of pRb in cycling cells in our model. This will better support our description of the Cdkn1c-Myc dynamics in relation with pRb. We therefore propose to reformulate this whole section as follows.
- It would be valuable to analyse the dynamics of Myc immunoreactivity in combination of pRb in all three gRNAs (highlighted in Supplementary Figure 1), as it would be a strong point in favour that the dynamics reflect the endogenous CDKN1c dynamics.
- It would be very valuable to provide a quantification of said dynamics (e.g. plotting myc intensity / pRb immunoreactivity along the apicobasal axis of the tissue).
These are two interesting suggestions. To complement our data with guide #1, we have performed Myc-immunostaining experiments on transverse sections in the context of guide #3, showing exactly the same pattern of Myc signal, with low expression in the VZ, and a peak of signal in the part of the mantle zone that is immediately touching the VZ. This confirms the specificity of the spatial distribution of the Cdkn1c-Myc signal. These data have been added in a revised version of Supplementary Figure 1.
We will perform the suggested quantifications using guides #1 and #3, which both show a good KI efficiency. We do not think it is useful to do these experiments with guide #2, whose efficiency is much lower, and which would lead to a very sparse signal.
- The characterization of dynamics is performed only with one of the gRNAs (#1) on the basis that it produces the strongest NLS-GFP signal, as a proxy for guide efficiency. It would be nice if the authors could validate guide cutting efficiency via sequencing (e.g. using a Cas9-T2A-GFP plasmid and sorting for positive cells).
We will perform these experiments to validate guide cutting efficiency using the Tide method (Brinkman et al, 2014)
- In order to make sure that the dynamics inferred from Myc-tag immunoreactivity do reflect the cell cycle dynamics of CDKN1c-myc, it would be advisable to confirm in-frame insertion of the myc-tag sequence.
We will perform genomic PCR experiments to confirm in-frame insertion of the Myc tags at the Cdkn1c locus
4.- In Figure 3, the authors use a short-hairpin-mediated knock-down strategy to decrease the levels of Cdkn1c, and show that this manipulation leads to an increase percentage of cycling progenitors and a decrease in the number of neurons in electroporated cells.
The authors claim that their shRNA-based knockdown strategy aims to reduce low-level Cdkn1c expression in neurogenic progenitors while minimally affecting the higher expression in newborn neurons required for cell cycle exit. However, several factors need consideration. Electroporation introduces variability in shRNA delivery, making it difficult to achieve consistent gene inhibition across all cells, especially for dose-dependent genes like Cdkn1c.
Additionally, Cdkn1c generates multiple isoforms, which may not be fully annotated in the chick genome, raising the possibility that the shRNA targets specific isoforms, potentially explaining the observed low expression.
All the predicted isoforms in the chick genome contain the sequence targeted by shRNA1, which is located in the CKI domain, the region of the protein that is most conserved between species. Besides, all the isoforms annotated in the mouse and human genomes also contain the region targeted by shRNA1. We are therefore confident that shRNA1 should target all chick isoforms.
A more rigorous approach, such as qPCR analysis of sorted electroporated cells, would better validate the expression levels, rather than relying on in situ hybridization, presenting electroporated and non-electroporated cells in the same section (Supp. Figure 2).
This approach (qRT-PCR on sorted cells) would enable us to focus solely on electroporated cells, but it would result in an averaged quantification of Cdkn1c depletion. In order to obtain additional information on the shRNA-dependent decrease in Cdkn1C in the different neural cell populations (progenitor versus differentiating neuron), we propose an alternative approach consisting in monitoring the level of Cdkn1c protein, assessed through Cdkn1c-Myc signal in knock-in cells, in the presence versus absence of Cdkn1c shRNA.
- As the authors note, "Unambiguous identification of cycling progenitors and postmitotic neurons is notoriously difficult in the chick spinal cord". "markers of progenitors usually either do not label all the phases of the cell cycle (eg. Phospho-Rb, thereafter pRb), or persist transiently in newborn neurons (eg. Sox2)." Given that pRb immunoreactivity is used as the basis for a lot of the conclusions in this study, it would be valuable to add a characterization of its dynamics as mentioned in Figure 2, as well as provide literary references/proof that Sox2 expression persists in newborn neurons.
We have addressed the case of pRb dynamics in progenitors above and added a reference documented pRb expression during the cell cycle of chick neural progenitors (Molina et al, 2022).
Regarding Sox2 persistence: we consistently detect a small fraction of double positive Sox2+/HuC/D+ cells in chick spinal cord transverse sections. We have shown that this marker of differentiating neurons (HuC/D) only becomes detectable more than 8 hours after mitosis in newborn neurons at E3 (Baek et al, 2018), indicating that Sox2 protein can persist for up to at least 8 hours in newborn neurons.
We now cite a paper showing that a similar persistence of Sox2 protein is reported in differentiating neurons of the human neocortex, where double Sox2/NeuN positive cells are frequently observed in cerebral organoids (Coquand et al, Nature Cell Biology 2024__)__
- The undefined population (pRb-/HuCD-) introduces an unknown that assumes that the percentage of progenitors in G1 phase before the restriction point and the number of newborn neurons are equal for both conditions in an experiment. Can the authors provide explanation for this assumption?
We do not think that these numbers are equal for both conditions, and we did not formulate this assumption. We only indicate (in the methods section) that this undefined/undetermined population (based on negativity for both markers) is a mix of two possible cell types. However, we do not offer any interpretation of the CDKN1c phenotypes based on the changes in this population. Indeed, our interpretation of the knock-down phenotype is solely based on the increase in pRb-positive and decrease in HuC/D-positive cells, which both suggest a delay in neurogenesis. We understand from the reviewer's comment that depicting an "undefined" population on the graph may cause some confusion. We therefore propose to present the data on pRb and HuC/D in different graphs, rather than on a combined plot, and to remove the reference to undefined cells in Figure 3, as well as in Figures 4 and 5 depicting the gain of function and double knock-down experiments. We have implemented these changes in updated versions of the figures.
- In Gui et al. (Dev Biol 2006), authors showed that a knockdown of Cdkn1c leads to a failure of nascent neurons to exit the cell cycle and causes them to re-entry the cell cycle, shown by ectopic mitoses. In that study, cells born from those ectopic mitoses eventually leave the cell cycle leading to an increase in the number of neurons. Can the authors check for ectopic mitoses at 24hpe and 48hpe?
We have now performed experiments with an anti phospho Histone 3 antibody, which labels mitotic cells, at 24 and 48 hours post electroporation. We do not see any ectopic mitoses upon Cdkn1c knock-down with this marker, and we have produced a Supplementary Figure with these data. This is consistent with the fact that we also do not see ectopic pRb or Sox2 positive cells in the mantle zone in the knock-down experiments. These data (pH3 and Sox2) have been added in the new Supplementary Figure 3E and F.
We have now modified the main text to include these data:
"In the context of a full knock-out of Cdkn1c in the mouse spinal cord, a reduction in neurogenesis was also observed, which was attributed to a failure of prospective neurons to exit the cell cycle, resulting in the observation of ectopic mitoses in the mantle zone (Gui et al, 2007). In contrast with this phenotype, using an anti phospho-Histone3 antibody, we did not observe any ectopic mitoses 24 or 48 hours after electroporation in our knock-down condition (Supplementary Figure 3E-F). This is consistent with the fact that we also do not observe ectopic cycling cells with pRb (Figure 3A and D) and Sox2 (Supplementary Figure 3E-F) antibodies. We therefore postulated that the reduced neurogenesis that we observe upon a partial Cdkn1c knock-down may result from a delayed transition of progenitors from the proliferative to neurogenic modes of division."
- The authors then address the question of whether the decrease in neuron number is due to the failure of newborn neurons to exit the cell cycle or to a delay in the transition from proliferative to neurogenic divisions. For that, they implement a strategy to label a synchronized cohort of progenitors based of incorporation of a FlashTag dye.
- Given that this strategy is the basis of many of the experiments in this article, it would be very valuable to expand on the validation of this technique as cited in major comment #2. In figure 3E, the close proximity of cell pairs in PP and PN clones shown in the pictures makes their sibling status apparent. However, this is not the case for the NN clone. Can the authors further explain with what criteria they determined the clonal status of two FlashTag labelled cells?
The key criterion for cells that are not directly touching each other is that their relative position corresponds to the classical "radial" organization of clones in this tissue (Leber and Sanes, 1995__; __Loulier et al, Neuron, 2014). In other words, we make sure that they are located on a same apico-basal axis, as is the case for the NN clone presented on the figure. As stated above in our response to major comment #2, we have modified the Methods section accordingly.
Can they provide further image examples of different types of clones?
We now provide additional examples in a new Supplementary Figure 4
- Can the authors show that the plateau reached in Sup Figure 3 for pRb immunoreactivity corresponds to a similar dynamic for HuC/D immunoreactivity?
The plateau for Rb phosphorylation in progenitors is reached before 6 hours post mitosis at E3. At the same age, we have previously shown (Baek et al, PLoS Biology 2018) in a similar time course experiment in pairs of FT+ cells that the HuC/D signal is not detected in newborn neurons 8 hours after mitosis. HuC/D only starts to appear between 8 and 12 hours, and still increases between 8 and 16 hours. The plateau would therefore be very delayed for HuC/D compared to pRb. This long delay in the appearance of this « positive » marker of neural differentiation is the main reason why we chose to use Rb phosphorylation status for the analysis of synchronous cohorts of pairs of sister cells, because pRb becomes a discriminating factor much earlier than HuC/D after mitosis.
- In order to further validate the strategy, could the authors use it at different stages to validate if they can replicate the different percentages of PP/PN/NN reported in the literature (e.g. Saade Cell Rep 2013)?
We have carried out similar experiments at E2, showing a plateau of 95% of pRb-positive cells in the FT-positive population (see graph on the right). This provides a retrospective estimate of the mode of division of the mother cells at this stage (roughly 90% of PP and 10% of PN) which is consistent with the vast majority of PP divisions described by Saade et al (2013, see Figure S1) at this stage.
5.- In Figure 4, the strategy used to induce a low-dose overexpression of CDKN1c is an elegant method to introduce CDKN1c-Myc expression under the control of the endogenous Pax7 promoter, active in proliferative progenitors. The main point to address is:
- Please provide proof that Pax7 expression is not altered in guides with a successful knock-in event (e.g. sorting and WB against the Pax7 protein) or the immunohistochemistry as performed in the Pax7-P2A-Gal4 tagging in Petit-Vargas et al., 2024.
We have now performed Pax7 immunostainings on transverse sections at 24 and 48 hours post electroporation, both with the Pax7-CDKN1c-Gal4 and with the Pax7-Gal4 control constructs. We present these data in the new supplementary figure 7. In both conditions, we find that the Pax7 protein is still present in KI-positive cells. We observe a modest increase in Pax7 signal intensity in these cells, suggesting either that the insertion of exogenous sequences stabilizes the Pax7 transcript, or that the C-terminal modification of Pax7 protein with the P2A tag increases its stability. This does not affect the interpretation of the CDKN1c overexpression phenotype, because we used the Pax7-Gal4 construct that shows the same modification of Pax7 stability as a control for this experiment. We have introduced this comment in the legend of Supplementary Figure 7.
- Given the cell cycle regulated expression and activity of CDKN1c, can the authors elaborate on whether this is regulated at the promoter level?
Cdkn1c transcription is regulated by multiple transcription factors and non-coding RNAs (see for example Creff and Besson, 2020, or Rossi et al, 2018 for a review). To our knowledge, these studies focus more on the regulation of Cdkn1c global expression than on the regulation of its levels during cell cycle progression. Although it is very likely that transcriptional regulation contributes, post-translational regulation, and in particular degradation by the proteasome, is also a key factor in the cell cycle regulation of Cdkn1c activity
If so, how does this differ from the promoter activity of Pax7?
The transcriptional regulation of Pax7 and Cdkn1c is probably controlled by different regulators, since their expression profiles are very different. Regardless of the mechanisms that control their expression, the rationale for choosing Pax7 as a driver for Cdkn1c expression was that Pax7 expression precedes that of Cdkn1c in the progenitor population, and that it disappears in newborn neurons, when that of Cdkn1c peaks. This provided us with a way to advance the timing of Cdkn1c expression onset in proliferative progenitors.
- It would be advisable to characterize the dynamics along the cell cycle for the overexpressed form of CDKN1c-Myc relative to pRb, similarly to what was done in Figure 2B.
We will carry out experiments similar to those shown in Figure 2B in order to characterise the dynamics of Cdkn1c in a context of overexpression, in relation to pRb.
In addition, we will include a more precise quantification of the "misexpressed" compared to "endogenous" Cdkn1c -Myc levels, as already mentioned in the answer to a request by reviewer1.
6.-In figure 5, the authors use a double knock-down strategy to test the hypothesis that the effect of Cdkn1c in G1 length is partially at least through its inhibition of CyclinD1. Results show that double shRNA-mediated knock-down of CyclinD1 and Cdkn1c counteracts the effects of Cdkn1c-sh alone on EdU incorporation, PP/PN/NN cell divisions and overall rations of progenitors and neurons.
- In the measurement of progenitor cell cycle length in Figure 5A, it would be more appropriate to present the nonlinear regression method described by Nowakowski et al. (1989), as has been commonly used in the field (Saade et al., 2013, PMID: 23891002, Le Dreau et al., 2014, PMID: 24515346, Arai et al., 2011, PMID: 21224845).
The Nowakowski non linear regression method has been used often in the literature in the same tissue, and is generally used to calculate fixed values for Tc, Ts, etc... This method is based on several selective criteria, and in particular the assumption that "all of the cells have the same cycle times". Yet, many studies have documented that cell cycle parameters change during the transition from proliferative to neurogenic modes of division during which our analysis is performed; live imaging data in the chick spinal cord have illustrated very different cell cycle durations at a given time point (see Molina et al). We therefore think that the proposed formulas do not reflect the heterogenous reality of neural progenitors of the embryonic spinal cord. However, the cumulative approach described by Nowakowski is useful to show qualitative differences between populations (e.g. a global decrease of the cycle length, like in our comparison between control and shRNA conditions). For these reasons, we prefer to display only the raw measurements rather than the regression curves.
- Cumulative EdU incorporation in spinal progenitors (pRb-positive) at E3 (24 hours after injection) showed that the proportion of EdU-positive progenitors reached a plateau at 14 hours in control conditions, which is later than what has been reported in Le Dreau et al., 2014 (PMID: 24515346). Can you explain why?
Le Dreau et al count the EdU+ proportion of cells in the total population of electroporated cells located in the VZ (which includes progenitors, but also future neurons that have been labelled during the previous cycles -at least for the time points after 2hours- and have not yet translocated to the mantle zone), whereas we only consider pRb+ progenitors in the analysis. In addition, the experiments are not performed at the same developmental stage. Altogether, this may account for the different curves obtained in our study.
- It would be interesting to measure G1 length as in Figure 5D for the double cdkn1c-sh - ccnd1-sh knock down condition, to see if it rescues G1 length. As well as in the Ccnd1 knock down condition alone to see if it increases G1 length in this context as well.
We will perform cumulative EDU incorporation experiments similar to that shown in Figure 5D to measure G1 length for the cdkn1c-sh - ccnd1-sh knock down double conditions, as well as in the Ccnd1 knock down condition alone.
Minor comments
__*Introduction:
- The introduction should include references of studies of the role of Cdkn1c in cortical development (Imaizumi et al. Sci Rep 2020, Colasante et al. Cereb Cortex 2015, Laukoter et al. ____Nature Communications 2020).*__
We will modify the introduction in several instances, in order to address suggestions by Reviewers #2 (see above) and #3, in particular to expand the description of the role of Cdkn1c during cortical development
1) Transcriptional signature of the neurogenic transition (Figure 1).
- In the result section, it would be informative to include the genes used to determine the progenitor and neuron score (instead of in Methods).
We have now listed the genes used to determine the progenitor and neuron score in the main text of the result section
- Figure 1A. It would be informative to add in the diagram what "filtering" means (eg. Neural crest cells).
We have now added the detail of what 'filtering' means in the diagram
- In the result section, "However, while Tis21 expression is switched off in neurons, Cdkn1c transiently peaks at high levels in nascent neurons before fading off in more mature cells." Missing literary reference or data to clearly demonstrate this point.
We have reworded this sentence, adding a reference to the expression profile of Tis 21. The paragraph now reads as follows:
« However, Cdkn1c expression is maintained longer and transiently peaks at high levels after Tis21 expression is switched off. Given that Tis21 is no more expressed in neurons (Iacopetti et al, 1999), this suggests that Cdkn1c expression is transiently upregulated in nascent neurons before fading off in more mature cells. »
- "Interestingly, the gene cluster that contained Tis21 also contained genes encoding proteins with known expression and/or functions at the transition from proliferation to differentiation, such as the Notch ligand Dll1, the bHLH transcription factors Hes6, NeuroG1 and NeuroG2, and the coactivator Gadd45g." Missing references.
We have now added references linking the function and/or expression profile of these genes to the neurogenic transition: Dll1 (Henrique et al., 1995), the bHLH transcription factors Hes6 (Fior and Henrique, 2005), NeuroG1 and NeuroG2 (Lacomme et al., 2012; Sommer et al., 1996) and the coactivator Gadd45g (Kawaue et al., 2014).
- There is an error in the color code in Cell Clusters in Figure 1C (cluster 4 yellow in the legend but ocre in the figure)
- Figure Sup3B colour code is switched (green for PP and red for NN) compared to the rest of the paper.
We have corrected the colour code errors in Figure 1c and Supp Figure 3B (now changed to Supplementary Figure 5 in the modified revision)
____It would be valuable to assign cell cycle stage to neural progenitor cells (based on cell cycle score) and determine whether cdkn1c at the transcript level also shows enrichment in G1 cells considered to be progenitors.
We have so far refrained from performing the suggested combined analysis based on cell cycle and cell type scores, as the "neurogenic progenitor population" (based on neurogenic progenitor score values) in which Cdkn1c expression is initiated represents a small number of cells in our scRNAseq, and felt that the significance of such an analysis is uncertain. We will perform this analysis in the revised version
2) Progressive increase in Cdkn1c/p57kip2 expression underlie different cellular states in the embryonic spinal neural tube (Figure 2).
- Figure 2A. Scale bar is missing in E3 and E4. It is important to consider the growth of the developing spinal cord and present it accordingly (E3 transverse section, Figure 2).
The scale bar is actually valid for the whole panel A. The E2 section in the original figure appeared as "large" as the E3 section along the DV axis probably because the cutting angle was not perfectly transverse at E2, artificially lengthening the section. In a new version of the figure, we have replaced the E2 images with another section from the same experiment. The scale bar remains valid for the whole panel.
- Figure 2 could use a diagram of the knock-in strategy used, similar as the one in Figure 4A.
We have now added a diagram for the knock-in strategy in Figure 2B, and modified the legend of the figure accordingly.
- Indicate hours post-electroporation. Indicate which guide is used in the main text.
We have now added the post-electroporation timing and guide used in the main text.
3) Downregulation of Cdkn1c in neural progenitors delays the transition from proliferative to neurogenic modes of division (Figure 3).
- In methods: "Thus, to reason on a more homogeneous progenitor population, we restricted all our analysis to the dorsal one half or two thirds of the neural tube." Indicate when and depending on what one half or two thirds of the neural tube were analysed.
- Are the clonal analysis experiments (Fig 3D, E and F) also restricted to the dorsal region?
__We have modified this sentence as follows: "__Thus, to reason on a more homogeneous progenitor population, we restricted all our analysis to the dorsal two thirds of the neural tube, except for the Pax7-Cdkn1c misexpression analysis, which was performed in the more dorsal Pax7 domain."
This is valid both for the whole population and clonal analyses
- Figure 3. Would have a better flow if 3C preceded 3A and 3B.
We have modified the Figure accordingly.
- Figure 3C. it would be informative to show pictures of the electroporated NT at both 24hpe and 48hpe, as well as highlighting the dorsal part of the neural tube that was used for quantification.
We have modified the Figure accordingly
- In methods "At each measured timepoint (1h, 4h, 7h, 10h, 12h, 14 and 17h after the first EdU injection), we quantified the number of EdU positive electroporated progenitors (triple positive for EdU, pRb and GFP) over the total population of electroporated progenitor cells (pRb and GFP positive) (Figure 3B)." Explanation does not correspond to Figure 3B.
This explanation corresponds indeed to Figure 5A. We have corrected this mistake in the new version of the manuscript.
4) Inducing a premature expression of Cdkn1c in progenitors triggers the transition to neurogenic modes of division (Figure 4.).
- "We took advantage of the Pax7 locus, which is expressed in progenitors in the dorsal domain at a level similar to that observed for Cdkn1c in neurogenic precursors (Supplementary Figure 4A)". Missing reference or data showing that Pax7 is restricted to the dorsal domain.
We have added references to the expression profile of Pax7 in the dorsal neural tube (Jostes et al, 1990). In addition, the new Supplementary Figure 7 shows anti-Pax7 staining that confirm this expression pattern at E3 and E4
- "its intensity was similar to the one observed for endogenous Myc-tagged Cdkn1c in progenitors (Figure 4B and Supplementary Figure 4E), and remained below the endogenous level of Myc-tagged Cdkn1c observed in nascent neurons, confirming the validity of our strategy". It would be valuable to add a quantification to demonstrate this point, either by fluorescence levels or WB of nls-GFP cells.
As stated in the response to Major Point 5 above, we will perform a quantification based on Myc immunofluorescence to compare endogenous Cdkn1c expression versus Cdkn1c expression upon overexpression.
- "At the population level, at E4, Cdkn1c expression from the Pax7 locus resulted in a strong reduction in the number of progenitors (pRb positive cells)". Indicate in the main text that this is 48hpe.
We have added in the main text that the quantification was performed 48hae.
- Legend of figure 4D should indicate that the quantification has been done 24hpe.
We have added the timing of quantification in the legend of Figure 4D.
- "To circumvent the cell cycle arrest that is triggered in progenitors by strong overexpression of Cdkn1c (Gui et al., 2007)". It would be advisable to expand on this reference on the text, or ideally to include a simple Cdkn1c overexpression experiment.
These experiments have been performed and presented in the study by Gui et al., 2007, which we cite in the paper. Using a strong overexpression of CDKN1c from the CAGGS promoter, they showed a massive decrease in proliferation, assessed by BrdU incorporation, 24hours after electroporation. We will cite this result more explicitly in the main text, and better explain the difference of our approach. We propose the following modification:
« We next explored whether low Cdkn1c activity is sufficient to induce the transition to neurogenic modes of division. A previous study has shown that overexpression of Cdkn1c driven by the strong CAGGS promoter triggers cell cycle exit of chick spinal cord progenitors, revealed by a drastic loss of BrdU incorporation 1 day after electroporation (Gui et al., 2007). As this precludes the exploration of our hypothesis, we developed an alternative approach designed to prematurely induce a pulse of Cdkn1c in progenitors, with the aim to emulate in proliferative progenitors the modest level of expression observed in neurogenic progenitors. We took advantage of the Pax7 locus, which is expressed in progenitors in the dorsal domain at a level similar to that observed for Cdkn1c in neurogenic precursors (Supplementary Figure 4A)."
- "We observed a massive increase in the proportion of neurogenic (PN and NN) divisions rising from 57% to 84% at the expense of proliferative pairs (43% PP pairs in controls versus 16% in misexpressing cells, Figure 4D)." adding the percentages in the main text is a bit inconsistent with how the rest of the data is presented in the rest of the sections.
This whole section has been modified in response to a question from reviewer 1. The new version does not contain percentages in the main text, and reads as follows:
« Using the FlashTag cohort labeling approach described above, we traced the fate of daughter cells born 24 hae. We observed an increase in the proportion of terminal neurogenic (NN) divisions and a decrease in proliferative (PP) divisions (Figure 4D). This suggests that CDKN1c premature expression in PP progenitors converts them to the PN mode of division, while the combined endogenous and Pax7-driven expression of CDKN1c converts PN progenitors to the NN mode of division. Coincidentally, at the stage analyzed, PP to PN conversions are balanced by PN to NN conversions, leaving the PN proportion artificially unchanged. The alternative interpretation of a direct conversion of symmetric PP into symmetric NN divisions is less likely, because the PN compartment was affected in the reciprocal CDKN1c shRNA approach (see Figure 3F). Overall, these data show that inducing a premature low-level expression of Cdkn1c in cycling progenitors is sufficient to accelerate the transition towards neurogenic modes of division. »
- Figure sup 4C includes references to 3 gRNAs even when only one is used in the study.
The three guides listed in the original Supplementary Figure 4C correspond to the guides that we tested in Petit-Vargas et al. 2024. In this study, we only used the most efficient of these three guides. We have modified Figure 4C by quoting only this guide.
5) The proneurogenic activity of Cdkn1c in progenitors is mediated by modulation of cell cycle dynamics (Figure 5)
- "we targeted the CyclinD1/CDK4-6 complex, which promotes cell cycle progression and proliferation, and is inhibited by Cdkn1c." reference missing
We have included references related to the activity of the CyclinD1/CDK4-6 complex in the developing CNS, and the antagonistic activities of CyclinD1 and Cdkn1c in this model
- "we targeted the CyclinD1/CDK4-6 complex, which promotes cell cycle progression and proliferation in the developing CNS (Lobjois et al, 2004, 2008, Lange 2009, Gui et al 2007), and is inhibited by Cdkn1c (Gui et al, 2007)."
- It would be informative to include experimental set-up information (e.g. hae) in Figures 5A, 5B, 5F and 5G.
We have added the experimental set-up information in Figure 5.
- Clarify if analysis is restricted to the dorsal progenitors or the whole dorsoventral length of the tube.
The analyses were carried out on two thirds of the neural tube (dorsal 2/3), excluding the ventral zone, as specified above (and in the Methods section)
- It would be valuable to add an image to illustrate what is quantified in Figure 5D, Figure F and Figure G.
- For Figure 4C and D, it would be valuable to add images to illustrate the quantification.
We have added images:
- in Supplementary Figure 7C to illustrate what is quantified in Figures 4C (now 4C and 4D);
- In Figure 5E to illustrate what is quantified in Figure 5D
- In Supplementary Figure 8B to illustrate what is quantified in Figure 5G (now Figure 5H and 5I) Regarding the requested images for Figures 4D and 5F, they correspond to the same types of images already shown in Figure 3E. Since we have now added several additional examples of representative pairs of each type of mode of division in the new Supplementary Figure 4, we do not think that adding more of these images in figures 4 and 5 would strengthen the result of the quantifications.
Discussion:
- "Nonetheless, studies in a wide range of species have demonstrated that beyond this binary choice, cell cycle regulators also influence the neurogenic potential of progenitors, i.e the commitment of their progeny to differentiate or not (Calegari and Huttner, 2003; FUJITA, 1962; Kicheva et al., 2014; Lange et al., 2009; Lukaszewicz and Anderson, 2011a; Pilaz et al., 2009; Smith and Schoenwolf, 1987; Takahashi et al., 1995)." Should include maybe references to Peco et al. Development 2012, Roussat et al. J Neurosci. 2023).
We have now included the references suggested by the reviewer.
- "This occurs through a change in the mode of division of progenitors, acting primarily via the inhibition of the CyclinD1/CDK6 complex." The data shown in the paper does not demonstrate that Cdkn1c is inhibiting CyclinD1, only that knocking down both mRNAs counteracts the effect of knocking down Cdkn1c alone at the general tissue level and in the percentage of PP/PN/NN clones. This statement should be qualified.
We propose to reformulate this paragraph in the discussion as follows to take this remark into account
"This allows us to re-interpret the role of Cdkn1c during spinal neurogenesis: while previously mostly considered as a binary regulator of cell cycle exit in newborn neurons, we demonstrate that Cdkn1c is also an intrinsic regulator of the transition from the proliferative to neurogenic status in cycling progenitors. This occurs through a change in their mode of division, and our double knock-down experiments suggest that the onset of Cdkn1c expression may promote this change by counteracting a CyclinD1/CDK6 complex dependent mechanism."
Other comments:
- To improve clarity for the reader, it would help if electroporation was shown consistently on the same side of the neural tube. If electroporation has been performed at different sides and this is reflected in the figures, it would be advisable to explain on the figure legend.
We have modified the figures to systematically show the electroporated side of the neural tube on the same side of the image for single electroporations.
____- Figure legends should include the number of embryos/tissue sections analysed for each experiment, as well as information on whether the sections were cryostat or vibratome.
This information is now provided in the figure legends (numbers of cells analysed and/or numbers of embryos), except for data in Figure 5, which are presented in a new Supplementary Table 1.
All experiments were performed on vibratome sections, except for in situ hybridization experiments, which were performed on cryostat sections. This last information was already indicated in the relevant figure legends
- Overall, there is a lack of consistency in the figures regarding how much information is available to the reader (e.g. Sup Figure 2A, in the panel mRNA in situ hybridisation of Cdkn1c is referred to only as Cdkn1c whereas in Sup figure 5 the in situ reads as CCND1 mRNA). Readability would improve a lot if figures included information on what is an electroporated fluorescent tag or an immunostaining (similar to the label in sup 4D) as well as the exact stage and hours after electroporation where relevant.
- There is a general lack of consistency in indicating the timing of the experiments, both in terms of embryonic stage/day and in terms of hours-post-electroporation.
We have now homogenized the nomenclature in the figures.
- "Primary antibodies used are: chick anti-GFP (GFP-1020 - 1:2000) from Aves Labs; goat antiSox2 (clone Y-17 - 1:1000) from Santa Cruz". There is no Sox2 immunostaining in the article.
In the original version of the manuscript, the anti-Sox2 antibody was not used; we have now added experiments using this antibody in the modified version of the manuscript; this sentence in the Methods thus remains unchanged.
Reviewer #3 (Significance (Required)):
__*Significance:
In neural development, there is a progressive switch in competence in neural progenitor cells, that transition from a proliferative (able to expand the neural progenitor pool) to neurogenic (able to produce neurons). Several factors are known to influence the transition of neural progenitor cells from a proliferative to a neurogenic state, including the activity of extracellular signalling pathways (e.g. SHH) (Saade et al. 2013, Tozer et al. 2017). In this study, the authors perform scRNA-seq of the cervical neural tube of chick at a stage of both proliferative and neurogenic progenitors are present, and identify transcriptional differences between the two populations. Among the differently expressed transcripts, they identify Cdkn1c (p57-Kip2) as enriched in neurogenic progenitors. Initially characterized as a driver of cell cycle exit in newborn neurons, the authors investigate the role of Cdkn1c in cycling progenitors. *__
The authors find that knock-down of Cdkn1c leads to an increase in proliferative divisions at the expense of neurogenic divisions. Conversely, misexpression of Cdkn1c in proliferative progenitors leads to a switch to neurogenic divisions. Furthermore, they find that knock-down of Cdkn1c shortens G1 phase of the cell cycle, suggesting a link between G1 length and neurogenic competence in neural progenitor cells. Cell cycle length has previously been linked to competence of neural progenitors, and it has been described that longer G1 duration is linked to neurogenic competence (e.g. Calegari F, Huttner WB. 2003).
The strengths of the study include:
The identification of a subset of genes enriched in neurogenic vs. proliferative progenitors. Since the transition from proliferative to neurogenic competence is a gradual process at the tissue level, the classification of proliferative vs. neurogenic progenitors based on a score of transcripts and the identification of a subset of transcripts that are enriched in neurogenic progenitors is a valuable contribution to the neurodevelopmental field.
- The somatic knock-in strategy used to induce low-level overexpression of Cdkn1c in proliferative progenitors is an elegant strategy to induce overexpression in a subset of cells in a controlled manner and is a valuable technical advance.
- The characterization of a specific role of Cdkn1c in regulating cell cycle length in cycling progenitors is novel and valuable knowledge contributing to our understanding of how regulation of cell cycle length impacts competence of neural progenitors.
The aspects to improve:
- The sc-RNAseq isolated genes enriched in neurogenic versus proliferative progenitors, providing valuable insight into the gradual transition from proliferative to neurogenic competence at the tissue level. However, this gene subset requires clearer representation and detailed characterization. Additionally, the full scRNA-seq dataset should be made publicly available to support further research in neurodevelopment.
The sequencing dataset has been deposited in NCBI's Gene Expression Omnibus database. It is currently under embargo, but will be made available upon acceptance and publication of the peer reviewed manuscript. Access is nonetheless available to the reviewers via a token that can be retrieved from the Review Commons website.
The following information will be added in the final manuscript.
Data availability
Single cell RNA sequencing data have been deposited in NCBI's Gene Expression Omnibus (GEO) repository under the accession number GSE273710, and are available at https://www.ncbi.nlm.nih.gov/geo/query/acc.cgi?acc=GSE273710."
- The characterization of Cdkn1c dynamics in cycling progenitors using endogenous tagging of the Cdkn1c transcript with a Myc tag is an elegant way to investigate the dynamics of Cdkn1c-myc along the cell cycle. However, it would be much more powerful if combined with a careful characterization of pRb immunostaining along the cell cycle in this tissue, as well as the quantifications and controls proposed. - Retinoblastoma protein (Rb) and cyclin D play a key role in regulating the G1/S transition, with cyclin D/CDK complexes phosphorylating Rb. Given that CDKN1c primarily inhibits the cyclin D/CDK6 complex, it likely affects pRb expression or phosphorylation. This suggests pRb may be a direct target of CDKN1c, making it an unreliable marker for tracking and quantifying neurogenic progenitors through CDKN1c modulation. In light of this, it would be more appropriate to consider pRb as a CDKN1c target and discuss the molecular mechanisms regulating cell cycle components. A more precise approach would involve using other markers or targets to quantify neural precursor division modes at earlier stages of neurogenesis.
- Many of the conclusions of the study are based on experiments performed using the FlashTag dye in order to perform clonal analysis of proliferative vs. neurogenic divisions. It would be very valuable to further characterize the reliability of this tool as well as to provide more information on the criteria used to determine the fate of the pairs of sister cells.
- The somatic knock-in strategy used to induce low-level overexpression of Cdkn1c in proliferative progenitors is an elegant strategy to induce overexpression in a subset of cells in a controlled manner. It would be valuable to further characterize the dynamics of Cdkn1c expression using this too and to provide proof that Pax7 expression is not altered in guides with the knock-in event.
- The presentation of the existing literature could be more up to date.
- The presentation of the data in the figures could be improved for readability. The sc-RNA seq data and the technical advances could be of interest for an audience of researchers using chick as a model organism, and working on neurodevelopment in general. Furthermore, the characterization of Cdkn1c as a regulator of G1 length in cycling progenitors and its implications for neurogenic competence could be of general interest for people working on basic research in the neurodevelopmental field.
Field of expertise of the reviewer: neural development, cell biology, embryology.
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Referee #3
Evidence, reproducibility and clarity
Summary:
In this study, Mida et al. analyze large-scale single-cell RNA-seq data from the chick embryonic neural tube and identify Cdkn1c as a key molecular regulator of the transition from proliferative to neurogenic cell divisions, marking the onset of neurogenesis in the developing CNS. To confirm this hypothesis, they employed classical techniques, including the quantification of neural cell-specific markers combined with the flashTAG label, to track and isolate isochronic cohorts of newborn cells in different division modes. Their findings reveal that Cdkn1c expression begins at low levels in neurogenic progenitors and becomes highly expressed in nascent neurons. Using a classical knockdown strategy based on short hairpin RNA (shRNA) interference, they demonstrate that Cdkn1c suppression promotes proliferative divisions, reducing neuron formation. Conversely, novel genetic manipulation techniques inducing low-level CDKN1c misexpression drive progenitors into neurogenic divisions prematurely. By employing cumulative EdU incorporation assays and shRNA-based loss-of-function approaches, Mida et al. further show that Cdkn1c extends the G1 phase by inhibiting cyclin D, ultimately concluding that Cdkn1c plays a dual role: first facilitating the transition of progenitors into neurogenic divisions at low expression levels, and later promoting cell cycle exit to ensure proper neural development.
This study presents several ambiguities and lacks precision in its analytical methodologies and quantification approaches, which contribute to confusion and potential bias. To enhance the reliability of the conclusions, a more rigorous validation of the methods employed is essential.
This study introduces a novel approach to tracking the fate of sister cells from neural progenitor divisions to infer the division modes. While previous methods for analyzing the division mode of neural progenitor cells have been implemented, rigorous validation of the approach introduced by Mida et al. is necessary. Furthermore, the concept of cell cycle regulators interacting to control the duration of specific cell cycle stages and influencing progenitor cell division modes has been explored before, potentially limiting the novelty of these findings.
Majors comments:
- The study presents ambiguity and lacks precision in quantifying neural precursor division modes. The authors use phosphorylated retinoblastoma protein (pRb) as a marker for neurogenic progenitors, claiming its reliability in identifying neurogenic divisions. However, they do not provide a thorough characterization of pRb expression in the developing chick neural tube, leaving its suitability as a neurogenic division marker unverified. Furthermore, retinoblastoma protein (Rb) and cyclin D interact crucially to regulate the G1/S phase transition of the cell cycle, with cyclin D/CDK complexes phosphorylating Rb. Since the authors conclude that CDKN1c primarily acts by inhibiting the cyclin D/CDK6 complex, it is likely that CDKN1c influences pRb expression or phosphorylation state. This raises the possibility that pRb could be a direct target of CDKN1c, whose expression and phosphorylation would be altered in gain-of-function (GOF) and loss-of-function (LOF) analyses of CDKN1c. In light of this, it would be more appropriate to consider pRb as a CDKN1c target and discuss the molecular mechanisms regulating cell cycle components. A more precise approach would involve using other markers or targets to quantify neural precursor division modes at earlier stages of neurogenesis.
- Furthermore, the study employs FlashTag labeling to track daughter cells post-division, but the 16-hour post-injection window may result in misidentification of sister cells due to the potential presence of FlashTagged cells that did not originate from the same division. This introduces a risk of bias in quantification, data misinterpretation, and potential errors in defining division modes. A more rigorous validation of the FlashTag strategy and its specificity in tracking division pairs is necessary to ensure the reliability of their conclusions.
- The knock-in strategy used to tag the endogenous CDKN1c protein in Figure 2 is an elegant tool to infer protein dynamics in vivo. However, since strong conclusions regarding CDKN1c dynamics during the cell cycle are drawn from this section, it would be advisable to strengthen the results by including quantification with adequate replication and proper statistical analysis, as the current findings are preliminary and somewhat speculative.
- "Although pRb is specific for cycling cells, it is only detected once cells have passed the point of restriction during the G1 phase." Please provide literary reference confirming this observation. Given that pRb immunoreactivity is used as a marker for cycling progenitors to base many of the results of this study, it would be very valuable to characterize the dynamics of pRb in cycling cells in the studied tissue, for instance combined with the cell cycle reporter used by Molina et al. (Development 2022).
- The characterization of dynamics is performed only with one of the gRNAs (#1) on the basis that it produces the strongest NLS-GFP signal, as a proxy for guide efficiency. It would be nice if the authors could validate guide cutting efficiency via sequencing (e.g. using a Cas9-T2A-GFP plasmid and sorting for positive cells).
- In order to make sure that the dynamics inferred from Myc-tag immunoreactivity do reflect the cell cycle dynamics of CDKN1c-myc, it would be advisable to confirm in-frame insertion of the myc-tag sequence.
- It would be valuable to analyse the dynamics of Myc immunoreactivity in combination of pRb in all three gRNAs (highlighted in Supplementary Figure 1), as it would be a strong point in favour that the dynamics reflect the endogenous CDKN1c dynamics.
- It would be very valuable to provide a quantification of said dynamics (e.g. plotting myc intensity / pRb immunoreactivity along the apicobasal axis of the tissue).
- In Figure 3, the authors use a short-hairpin-mediated knock-down strategy to decrease the levels of Cdkn1c, and show that this manipulation leads to an increase percentage of cycling progenitors and a decrease in the number of neurons in electroporated cells.
The authors claim that their shRNA-based knockdown strategy aims to reduce low-level Cdkn1c expression in neurogenic progenitors while minimally affecting the higher expression in newborn neurons required for cell cycle exit. However, several factors need consideration. Electroporation introduces variability in shRNA delivery, making it difficult to achieve consistent gene inhibition across all cells, especially for dose-dependent genes like Cdkn1c. Additionally, Cdkn1c generates multiple isoforms, which may not be fully annotated in the chick genome, raising the possibility that the shRNA targets specific isoforms, potentially explaining the observed low expression. A more rigorous approach, such as qPCR analysis of sorted electroporated cells, would better validate the expression levels, rather than relying on in situ hybridization, presenting electroporated and non-electroporated cells in the same section (Supp. Figure 2). - As the authors note, "Unambiguous identification of cycling progenitors and postmitotic neurons is notoriously difficult in the chick spinal cord". "markers of progenitors usually either do not label all the phases of the cell cycle (eg. Phospho-Rb, thereafter pRb), or persist transiently in newborn neurons (eg. Sox2)." Given that pRb immunoreactivity is used as the basis for a lot of the conclusions in this study, it would be valuable to add a characterization of its dynamics as mentioned in Figure 2, as well as provide literary references/proof that Sox2 expression persists in newborn neurons. - The undefined population (pRb-/HuCD-) introduces an unknown that assumes that the percentage of progenitors in G1 phase before the restriction point and the number of newborn neurons are equal for both conditions in an experiment. Can the authors provide explanation for this assumption? - In Gui et al. (Dev Biol 2006), authors showed that a knockdown of Cdkn1c leads to a failure of nascent neurons to exit the cell cycle and causes them to re-entry the cell cycle, shown by ectopic mitoses. In that study, cells born from those ectopic mitoses eventually leave the cell cycle leading to an increase in the number of neurons. Can the authors check for ectopic mitoses at 24hpe and 48hpe? - The authors then address the question of whether the decrease in neuron number is due to the failure of newborn neurons to exit the cell cycle or to a delay in the transition from proliferative to neurogenic divisions. For that, they implement a strategy to label a synchronized cohort of progenitors based of incorporation of a FlashTag dye. - Given that this strategy is the basis of many of the experiments in this article, it would be very valuable to expand on the validation of this technique as cited in major comment #2. In figure 3E, the close proximity of cell pairs in PP and PN clones shown in the pictures makes their sibling status apparent. However, this is not the case for the NN clone. Can the authors further explain with what criteria they determined the clonal status of two FlashTag labelled cells? Can they provide further image examples of different types of clones? - Can the authors show that the plateau reached in Sup Figure 3 for pRb immunoreactivity corresponds to a similar dynamic for HuC/D immunoreactivity? - In order to further validate the strategy, could the authors use it at different stages to validate if they can replicate the different percentages of PP/PN/NN reported in the literature (e.g. Saade Cell Rep 2013)?. 5. In Figure 4, the strategy used to induce a low-dose overexpression of CDKN1c is an elegant method to introduce CDKN1c-Myc expression under the control of the endogenous Pax7 promoter, active in proliferative progenitors. The main point to address is: - Please provide proof that Pax7 expression is not altered in guides with a successful knock-in event (e.g. sorting and WB against the Pax7 protein) or the immunohistochemistry as performed in the Pax7-P2A-Gal4 tagging in Petit-Vargas et al., 2024. - Given the cell cycle regulated expression and activity of CDKN1c, can the authors elaborate on whether this is regulated at the promoter level? If so, how does this differ from the promoter activity of Pax7? - It would be advisable to characterize the dynamics along the cell cycle for the overexpressed form of CDKN1c-Myc relative to pRb, similarly to what was done in Figure 2B. 6. In figure 5, the authors use a double knock-down strategy to test the hypothesis that the effect of Cdkn1c in G1 length is partially at least through its inhibition of CyclinD1. Results show that double shRNA-mediated knock-down of CyclinD1 and Cdkn1c counteracts the effects of Cdkn1c-sh alone on EdU incorporation, PP/PN/NN cell divisions and overall rations of progenitors and neurons. - In the measurement of progenitor cell cycle length in Figure 5A, it would be more appropriate to present the nonlinear regression method described by Nowakowski et al. (1989), as has been commonly used in the field (Saade et al., 2013, PMID: 23891002, Le Dreau et al., 2014, PMID: 24515346, Arai et al., 2011, PMID: 21224845). - Cumulative EdU incorporation in spinal progenitors (pRb-positive) at E3 (24 hours after injection) showed that the proportion of EdU-positive progenitors reached a plateau at 14 hours in control conditions, which is later than what has been reported in Le Dreau et al., 2014 (PMID: 24515346). Can you explain why? - It would be interesting to measure G1 length as in Figure 5D for the double cdkn1c-sh - ccnd1-sh knock down condition, to see if it rescues G1 length. As well as in the Ccnd1 knock down condition alone to see if it increases G1 length in this context as well.
Minor comments
Introduction:
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The introduction should include references of studies of the role of Cdkn1c in cortical development (Imaizumi et al. Sci Rep 2020, Colasante et al. Cereb Cortex 2015, Laukoter et al. Nature Communications 2020).
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Transcriptional signature of the neurogenic transition (Figure 1).
- In the result section, it would be informative to include the genes used to determine the progenitor and neuron score (instead of in Methods).
- Figure 1A. It would be informative to add in the diagram what "filtering" means (eg. Neural crest cells).
- In the result section, "However, while Tis21 expression is switched off in neurons, Cdkn1c transiently peaks at high levels in nascent neurons before fading off in more mature cells." Missing literary reference or data to clearly demonstrate this point.
- "Interestingly, the gene cluster that contained Tis21 also contained genes encoding proteins with known expression and/or functions at the transition from proliferation to differentiation, such as the Notch ligand Dll1, the bHLH transcription factors Hes6, NeuroG1 and NeuroG2, and the coactivator Gadd45g." Missing references.
- There is an error in the color code in Cell Clusters in Figure 1C (cluster 4 yellow in the legend but ocre in the figure)
It would be valuable to assign cell cycle stage to neural progenitor cells (based on cell cycle score) and determine whether cdkn1c at the transcript level also shows enrichment in G1 cells considered to be progenitors. 2. Progressive increase in Cdkn1c/p57kip2 expression underlie different cellular states in the embryonic spinal neural tube (Figure 2). - Figure 2A. Scale bar is missing in E3 and E4. It is important to consider the growth of the developing spinal cord and present it accordingly (E3 transverse section, Figure 2). - Figure 2 could use a diagram of the knock-in strategy used, similar as the one in Figure 4A. - Indicate hours post-electroporation. Indicate which guide is used in the main text. 3. Downregulation of Cdkn1c in neural progenitors delays the transition from proliferative to neurogenic modes of division (Figure 3). - In methods: "Thus, to reason on a more homogeneous progenitor population, we restricted all our analysis to the dorsal one half or two thirds of the neural tube." Indicate when and depending on what one half or two thirds of the neural tube were analysed. - Figure 3. Would have a better flow if 3C preceded 3A and 3B. - Figure 3C. it would be informative to show pictures of the electroporated NT at both 24hpe and 48hpe, as well as highlighting the dorsal part of the neural tube that was used for quantification. - Are the clonal analysis experiments (Fig 3D, E and F) also restricted to the dorsal region? - Figure Sup3B colour code is switched (green for PP and red for NN) compared to the rest of the paper. - In methods "At each measured timepoint (1h, 4h, 7h, 10h, 12h, 14 and 17h after the first EdU injection), we quantified the number of EdU positive electroporated progenitors (triple positive for EdU, pRb and GFP) over the total population of electroporated progenitor cells (pRb and GFP positive) (Figure 3B)." Explanation does not correspond to Figure 3B. 4. Inducing a premature expression of Cdkn1c in progenitors triggers the transition to neurogenic modes of division (Figure 4.).<br /> - "We took advantage of the Pax7 locus, which is expressed in progenitors in the dorsal domain at a level similar to that observed for Cdkn1c in neurogenic precursors (Supplementary Figure 4A)". Missing reference or data showing that Pax7 is restricted to the dorsal domain. - "its intensity was similar to the one observed for endogenous Myc-tagged Cdkn1c in progenitors (Figure 4B and Supplementary Figure 4E), and remained below the endogenous level of Myc-tagged Cdkn1c observed in nascent neurons, confirming the validity of our strategy". It would be valuable to add a quantification to demonstrate this point, either by fluorescence levels or WB of nls-GFP cells. - For Figure 4C and D, it would be valuable to add images to illustrate the quantification. - "At the population level, at E4, Cdkn1c expression from the Pax7 locus resulted in a strong reduction in the number of progenitors (pRb positive cells)". Indicate in the main text that this is 48hpe. - Legend of figure 4D should indicate that the quantification has been done 24hpe. - "To circumvent the cell cycle arrest that is triggered in progenitors by strong overexpression of Cdkn1c (Gui et al., 2007)". It would be advisable to expand on this reference on the text, or ideally to include a simple Cdkn1c overexpression experiment. - "We observed a massive increase in the proportion of neurogenic (PN and NN) divisions rising from 57% to 84% at the expense of proliferative pairs (43% PP pairs in controls versus 16% in misexpressing cells, Figure 4D)." adding the percentages in the main text is a bit inconsistent with how the rest of the data is presented in the rest of the sections. - Figure sup 4C includes references to 3 gRNAs even when only one is used in the study. 5. The proneurogenic activity of Cdkn1c in progenitors is mediated by modulation of cell cycle dynamics (Figure 5) - "we targeted the CyclinD1/CDK4-6 complex, which promotes cell cycle progression and proliferation, and is inhibited by Cdkn1c." reference missing - It would be valuable to add an image to illustrate what is quantified in Figure 5D, Figure F and Figure G. - It would be informative to include experimental set-up information (e.g. hae) in Figures 5A, 5B, 5F and 5G. - Clarify if analysis is restricted to the dorsal progenitors or the whole dorsoventral length of the tube.
Discussion:
- "Nonetheless, studies in a wide range of species have demonstrated that beyond this binary choice, cell cycle regulators also influence the neurogenic potential of progenitors, i.e the commitment of their progeny to differentiate or not (Calegari and Huttner, 2003; FUJITA, 1962; Kicheva et al., 2014; Lange et al., 2009; Lukaszewicz and Anderson, 2011a; Pilaz et al., 2009; Smith and Schoenwolf, 1987; Takahashi et al., 1995)." Should include maybe references to Peco et al. Development 2012, Roussat et al. J Neurosci. 2023).
- "This occurs through a change in the mode of division of progenitors, acting primarily via the inhibition of the CyclinD1/CDK6 complex." The data shown in the paper does not demonstrate that Cdkn1c is inhibiting CyclinD1, only that knocking down both mRNAs counteracts the effect of knocking down Cdkn1c alone at the general tissue level and in the percentage of PP/PN/NN clones. This statement should be qualified.
Other comments:
- There is a general lack of consistency in indicating the timing of the experiments, both in terms of embryonic stage/day and in terms of hours-post-electroporation.
- To improve clarity for the reader, it would help if electroporation was shown consistently on the same side of the neural tube. If electroporation has been performed at different sides and this is reflected in the figures, it would be advisable to explain on the figure legend.
- Figure legends should include the number of embryos/tissue sections analysed for each experiment, as well as information on whether the sections were cryostat or vibratome.
- Overall, there is a lack of consistency in the figures regarding how much information is available to the reader (e.g. Sup Figure 2A, in the panel mRNA in situ hybridisation of Cdkn1c is referred to only as Cdkn1c whereas in Sup figure 5 the in situ reads as CCND1 mRNA). Readability would improve a lot if figures included information on what is an electroporated fluorescent tag or an immunostaining (similar to the label in sup 4D) as well as the exact stage and hours after electroporation where relevant.
- "Primary antibodies used are: chick anti-GFP (GFP-1020 - 1:2000) from Aves Labs; goat antiSox2 (clone Y-17 - 1:1000) from Santa Cruz". There is no Sox2 immunostaining in the article.
Significance
In neural development, there is a progressive switch in competence in neural progenitor cells, that transition from a proliferative (able to expand the neural progenitor pool) to neurogenic (able to produce neurons). Several factors are known to influence the transition of neural progenitor cells from a proliferative to a neurogenic state, including the activity of extracellular signalling pathways (e.g. SHH) (Saade et al. 2013, Tozer et al. 2017). In this study, the authors perform scRNA-seq of the cervical neural tube of chick at a stage of both proliferative and neurogenic progenitors are present, and identify transcriptional differences between the two populations. Among the differently expressed transcripts, they identify Cdkn1c (p57-Kip2) as enriched in neurogenic progenitors. Initially characterized as a driver of cell cycle exit in newborn neurons, the authors investigate the role of Cdkn1c in cycling progenitors. The authors find that knock-down of Cdkn1c leads to an increase in proliferative divisions at the expense of neurogenic divisions. Conversely, misexpression of Cdkn1c in proliferative progenitors leads to a switch to neurogenic divisions. Furthermore, they find that knock-down of Cdkn1c shortens G1 phase of the cell cycle, suggesting a link between G1 length and neurogenic competence in neural progenitor cells. Cell cycle length has previously been linked to competence of neural progenitors, and it has been described that longer G1 duration is linked to neurogenic competence (e.g. Calegari F, Huttner WB. 2003).
The strengths of the study include:
The identification of a subset of genes enriched in neurogenic vs. proliferative progenitors. Since the transition from proliferative to neurogenic competence is a gradual process at the tissue level, the classification of proliferative vs. neurogenic progenitors based on a score of transcripts and the identification of a subset of transcripts that are enriched in neurogenic progenitors is a valuable contribution to the neurodevelopmental field.
- The somatic knock-in strategy used to induce low-level overexpression of Cdkn1c in proliferative progenitors is an elegant strategy to induce overexpression in a subset of cells in a controlled manner and is a valuable technical advance.
- The characterization of a specific role of Cdkn1c in regulating cell cycle length in cycling progenitors is novel and valuable knowledge contributing to our understanding of how regulation of cell cycle length impacts competence of neural progenitors.
The aspects to improve:
- The sc-RNAseq isolated genes enriched in neurogenic versus proliferative progenitors, providing valuable insight into the gradual transition from proliferative to neurogenic competence at the tissue level. However, this gene subset requires clearer representation and detailed characterization. Additionally, the full scRNA-seq dataset should be made publicly available to support further research in neurodevelopment.
- The characterization of Cdkn1c dynamics in cycling progenitors using endogenous tagging of the Cdkn1c transcript with a Myc tag is an elegant way to investigate the dynamics of Cdkn1c-myc along the cell cycle. However, it would be much more powerful if combined with a careful characterization of pRb immunostaining along the cell cycle in this tissue, as well as the quantifications and controls proposed.
- Retinoblastoma protein (Rb) and cyclin D play a key role in regulating the G1/S transition, with cyclin D/CDK complexes phosphorylating Rb. Given that CDKN1c primarily inhibits the cyclin D/CDK6 complex, it likely affects pRb expression or phosphorylation. This suggests pRb may be a direct target of CDKN1c, making it an unreliable marker for tracking and quantifying neurogenic progenitors through CDKN1c modulation. In light of this, it would be more appropriate to consider pRb as a CDKN1c target and discuss the molecular mechanisms regulating cell cycle components. A more precise approach would involve using other markers or targets to quantify neural precursor division modes at earlier stages of neurogenesis.
- Many of the conclusions of the study are based on experiments performed using the FlashTag dye in order to perform clonal analysis of proliferative vs. neurogenic divisions. It would be very valuable to further characterize the reliability of this tool as well as to provide more information on the criteria used to determine the fate of the pairs of sister cells.
- The somatic knock-in strategy used to induce low-level overexpression of Cdkn1c in proliferative progenitors is an elegant strategy to induce overexpression in a subset of cells in a controlled manner. It would be valuable to further characterize the dynamics of Cdkn1c expression using this too and to provide proof that Pax7 expression is not altered in guides with the knock-in event.
- The presentation of the existing literature could be more up to date.
- The presentation of the data in the figures could be improved for readability. The sc-RNA seq data and the technical advances could be of interest for an audience of researchers using chick as a model organism, and working on neurodevelopment in general. Furthermore, the characterization of Cdkn1c as a regulator of G1 length in cycling progenitors and its implications for neurogenic competence could be of general interest for people working on basic research in the neurodevelopmental field.
Field of expertise of the reviewer: neural development, cell biology, embryology.
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Referee #2
Evidence, reproducibility and clarity
The work by Mida and colleagues addresses important questions about neurogenesis in the embryo, using the chicken neural tube as their model system. The authors investigate the mechanisms involved in the transition from stem cell self-renewal to neurogenic progenitor divisions, using a combination of single cell, gene functional and tracing studies.
The authors generated a new single cell data set from the embryonic chicken spinal cord and identify a transitory cell population undergoing neuronal differentiation, which expresses Tis21, Neurog2 and Cdkn1c amongst other genes. They then study the role of Cdkn1c and investigate the hypothesis that it plays a dual role in spinal cord neurogenesis: low levels favour transition from proliferative to neurogenic divisions and high levels drive cell cycle exit and neuronal differentiation.
Major comments
I have only a general comment related to the main point of the paper. The authors claim that Cdkn1c onset in cycling progenitor drives transition towards neurogenic modes of division, which is different from its role in cell cycle exit and differentiation. Figures 3F and 4D are key figures where the authors analysed PP, PN and NN mode of divisions via flash tag followed by analysis of sister cell fate. If their assumption is correct, shouldn't they also see, for example in Fig. 4D, an increase in PN or is this too transient to be observed or is it bypassed? At the moment, the calculations of PN and NN frequencies are merged in the text, so perhaps describing PN and NN numbers separately will help better understand the dynamics of this gradual process (especially since there is little to no difference in PN). Could the increase in NN be compatible also with a role in cell cycle exit and differentiation, for example from cells that have been targeted and are still undergoing the last division (hence marked by flash tag) or there won't be any GFP cells marked by flash tag a day after expression of high levels of Cdkn1c? Basically, what would the effect of expressing higher levels of Cdkn1c be? I guess this will really help them distinguish between transition to neurogenic division rather than neuronal differentiation. If not experimentally, any further comments on this would be appreciated.
Minor comments
Fig 3C my understanding is that HuC/D should be nuclear, but in fig 3C it seems more cytoplasmic (any comment?)
Fig Suppl 3E (and related 4B), immuno for Cdkn1c-Myc: to help the reader understand the difference between the immuno signals when looking at the figure, I would suggest writing on the panel i) Pax7-Cdkn1c-Myc and ii) endogenous Cdkn1c-Myc, rather than 'misexpressed' and 'endogenous', which is slightly confusing (especially because what it is called endogenous expression is higher).
Literature citing: Introduction and discussion are very nicely written, although they could benefit from some more recent literature on the topic. For example, Cdkn1c role as a gatekeeper of stem cell reserve in the stomach, gut, (Lee et al, CellStemCell 2022 PMID: 35523142) or some other work on symmetric/asymmetric divisions and clonal analysis in zebrafish (Hevia et al, CellRep 2022 PMID: 35675784, Alexandre et al, NatNeur PMID: 20453852), mammals (Royal et al, Elife 2023 37882444, Appiah et al, EMBO rep 2023 PMID: 37382163). Also, similar work has been performed in the developing pancreatic epithelium, where mild expression of Cdkn1a under Sox9rtTa control was used to lengthen G1 without overt cell cycle exit and this resulted in Neurog3 stabilization and priming for endocrine differentiation (Krentz et al, DevCell 2017 PMID: 28441528), so similar mechanisms might be in in place to gradually shift progenitor towards stable decision to differentiate. Moreover, in the discussion, alongside Neurog2 control of Cdkn1c, it could be mentioned that the feedback loop between Cdk inhibitors and neurogenic factor is usually established via Cdk inhibitor-mediated inhibition of proneural bHLHs phosphorylation by CDKs (Krentz et al, DevCell 2017 PMID: 28441528, Ali et al, 24821983, Azzarelli et al 2017 - PMID: 28457793; 2024 - PMID:39575884). Further, in the discussion, could they mention anything about the following open questions: is there evidence for Cdkn1c low/high expression in mammalian spinal cord? Or maybe of other Cdk inhibitors? Is Cdkn1c also involved in cell cycle exit during gliogenesis or is there another Cdk inhibitor expressed at later developmental stages, hence linking this with specific cell fate decisions?
Significance
The work here presented has important implications on neural development and its disorders. The authors used the most advanced technologies to perform gene functional studies, such as CRISPR-HDR insertion of Myc-tag to follow endogenous expression, or expression under endogenous Pax7 promoter, often followed by flash tag experiments to trace sister cell fate, and all of this in an in vivo system. They then tested cell cycle parameters, clonal behaviour and modes of cell division in a very accurate way. Overall data are convincing and beautifully presented. The limitation is potentially in the resolution between the events of switching to neurogenic division versus neuronal differentiation, which might just warrant further discussion. This work advances our knowledge on vertebrate neurogenesis, by investigating a key player in proliferation and differentiation.
I believe this work will be of general interest to developmental and cellular biologists in different fields. Because it addresses fundamental questions about the coordination between cell cycle and differentiation and fate decision making, some basic concepts can be translated to other tissues and other species, thus increasing the potential interested audience.
My work focuses on stem cell fate decisions in mammalian systems, and I am familiar with the molecular underpinnings of the work here presented. However, I am not an expert in the chicken spinal cord as a model and yet the manuscript was interesting. I am also not sufficiently expert in the bioinformatic analysis, so cannot comment on the technical aspects of Figure 1 and the way they decided to annotate their data.
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Referee #1
Evidence, reproducibility and clarity
Summary
This study utilizes the developing chicken neural tube to assess the regulation of the balance between proliferative and neurogenic divisions in the vertebrate CNS. Using single-cell RNAseq and endogenous protein tagging, the authors identify Cdkn1c as a potential regulator of the transition towards neurogenic divisions. Cdkn1c knockdown and overexpression experiments suggest that low Cdkn1c expression enhances neurogenic divisions. Using a combination of clonal analysis and sequential knockdown, the authors find that Cdkn1c lengthens the G1 phase of the cell cycle via inhibition of cyclinD1. This study represents a significant advance in understanding how cells can transition between proliferative and asymmetric modes of division, the complex and varying roles of cycle regulators, and provides technical advance through innovative combination of existing tools.
Major and Minor Comments:
Overall
- Sample numbers are missing or unclear throughout for all imaging experiments. The authors should add numbers of cells analysed and/or numbers of embryos for their results to be appropriately convincing.
- Values and error bars on graphs must be defined throughout. Are the values means and error bars SD or SEM?
Results 2
- A reference should be provided for cell type distribution in spinal neural tube, where the authors state that cell bodies of progenitors reside within the ventricular zone.
- The authors state that Cdkn1c "was expressed at low levels in a salt and pepper fashion in the ventricular zone, where the cell bodies of neural progenitors reside, and markedly increased in a domain immediately adjacent to this zone which is enriched in nascent neurons on their way to the mantle zone. In contrast, the transcript was completely excluded from the mantle zone, where HuC/D positive mature neurons accumulate." It is not clear if this is referring only to E4 or also to E3 embryos. Indeed, Cdkn1c expression appears to be much more salt and pepper at E3 and only resolves into a clear domain of high expression adjacent to the mantle zone at E4. It may be helpful if this expression pattern could be described in a bit more detail highlighting the changes that occur between E3 and E4.
- It would be useful to annotate the ISH images in Fig 2A to show the ventricular and mantle zones as defined by immunofluorescence.
- Reference should be included for pRb expression dynamics.
- Could the Myc tag insertion approach disrupt protein function or turnover?
- Why was the insertion target site at the C terminus chosen?
- OPTIONAL Could a similar approach be used to tag Cdkn1c with a fluorescent protein to enable live imaging of dynamics?
- In suppl Fig 1C nlsGFP-positive cells are shown in the control shRNA condition. How can this be explained and does it impact the interpretation of the findings?
- In Fig 2B, there are a number of Myc labelled cells in the mantle zone, whereas the in situ images show no appreciable transcript expression. Is this because the protein but not the transcript is present in these cells? Could the authors comment on this?
Results 3
- It should be mentioned how mRNA expression levels were quantified in the shRNA validation experiment (supp Fig 2A).
- Figure panels are not currently cited in order. Citation or figure order could be changed.
- The authors should provide representative images for the graphs shown in Fig 3A and 3B. These could go into supplementary if the authors prefer.
- A supplementary figure showing the Caspase3 experiment should be added.
- OPTIONAL. Identification of sister cells in the clonal analysis experiments is based on static images and cannot be guaranteed. Could live imaging be used to watch divisions followed by fixation and immunostaining to confirm identity?
Results 4
- How did the authors quantify the intensity of endogenous Myc-tagged Cdkn1c to confirm the validity of the Pax7 locus knock in? Can they show that the expression level was consistently lower than the endogenous expression in neurons? Quantification and sample numbers should be shown.
- In Fig 4B, the brightness of row 2 column 1 is lower than the same image in row 2 column 2, which is slightly misleading, since it makes the misexpressed expression level look lower than it is compared with endogenous in column 3. Is this because only a single z-section is being displayed in the zoomed in image? If so, this should be stated in the figure legend.
- In Fig 4D, the increase in neurogenic divisions is mainly because of the rise in terminal NN divisions according to the graph, but no clear increase in PN divisions. Could the authors comment on the significance of this?
Results 5
- The proportion of pRb-positive progenitors having entered S phase was stated to be higher at all time points; however, it is not significantly higher until 6h30 and is actually trending lower at 2h30.
- OPTIONAL Could CyclinD1 activity be directly assessed?
General
- Scale bars missing fig s1c s4d.
- OPTIONAL Some of the main findings be replicated in another species, for example, mouse or human to examine whether the mechanism is conserved.
- OPTIONAL Could use approaches other than image analysis be used to reinforce findings, for example biochemical methods, RNAseq or FACS?
- A model cartoon to summarise outcomes would be useful.
- Unclear how cells were determined to be positive or negative for a label. Was this decided by eye? If so, how did the authors ensure that this was unbiased?
Significance
Strengths:
This manuscript investigates the mechanisms regulating the switch from symmetric proliferative divisions to neurogenic division during vertebrate neuronal differentiation. This is a question of fundamental importance, the answer to which has eluded us so far. As such, the findings presented here are of significant value to the neurogenesis community and will be of broad interest to those interested in cell divisions and asymmetric cell fate acquisition. Specific strengths include:
- Variety of approaches used to manipulate and observe individual cell behaviour within a physiological context.
- A limitation of using the chicken embryo is the lack of available antibodies for immunostaining. The authors take advantage of recent advances in chicken embryo CRISPR strategy to endogenously tag the target protein with Myc, to facilitate immunostaining.
- Innovative combination of genetic and labelling tools to target cells, for example, use of FlashTag and EdU in combination to more accurately assess G1 length than the more commonly used method.
- Premature misexpression demonstrates that the previously observed dynamics indeed regulate cell fate.
- Mechanistic insight by examining downstream target CyclinD1.
- Clearly presented with useful illustrations throughout.
- Logic is clear and examination thorough.
- Conclusions are warranted on the basis of their findings.
Limitations
- This study primarily used visual analysis of fixed tissue images to assess the main outcomes. To reinforce the conclusions, these could be supplemented with live imaging to appreciate dynamics, or biochemical techniques to look at protein expression levels.
- Some aspects of quantification require explanation in order for the experiments to be replicated.
- It is imperative that precise sample sizes are included for all experiments presented.
Advance:
- First functional demonstration role for Cdkn1c in regulating neurogenic transition in progenitors.
- Conceptual advance suggesting Cdkn1c has dual roles in driving neurogenesis: promoting neurogenic divisions of progenitors and the established role of mediating cell cycle exit previously reported.
- Technical advances in the form of G1 signposting and endogenous Myc tagging using CRISPR in chicken embryonic tissue.
Audience:
Of broad interest to developmental biologists. Could be relevant to cancer, since Cdkn1c is implicated.
Please define your field of expertise with a few keywords to help the authors contextualize your point Developmental biology, vertebrate embryonic development, neuronal differentiation, imaging. Please note that we have not commented on RNAseq experiments as these are outside of our area of expertise.
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learn.cantrill.io learn.cantrill.io
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Welcome back and in this video I want to talk about geolocation routing which is another routing policy available within Route 53. Now this is going to be a pretty brief video so let's jump in and get started.
In many ways geolocation routing is similar to latency, only instead of latency, the location of customers and the location of resources are used to influence resolution decisions. With geolocation routing, when you create records you tag the records with the location. Now this location is generally a country, so using ISO standard country codes, it can be continents—again using ISO continent codes such as SA for South America in this case—or records can be tagged with default. Now there's a fourth type which is known as a subdivision; in America you can tag records with the state that the record belongs to.
Now when a user is making a resolution request, an IP check verifies the location of the user. Depending on the DNS system, this can be the user directly or the resolver server, but in most cases these are one and the same in terms of the user's location. So we have the location of the user and we have the location of the records. What happens next is important because geolocation doesn't return the closest record, it only returns relevant records.
When a resolution request happens, Route 53 takes the location of the user and it starts checking for any matching records. First, if the user doing the resolution request is based in the US, then it checks the state of the user and it tries to match any records which have a state allocated to them. If any records match, they're returned and the process stops. If no state records match, then it checks the country of the user. If any records are tagged with that country, then they're returned and the process stops. Then it checks the continent; if any records match the continent that the user is based in, then they're returned and the process stops.
Now you can also define a default record which is returned if no record is relevant for that user. If nothing matches though—so there are no records that match the user's location and there's no default record—then a no answer is returned. So to stress again, this type of routing policy does not return the closest record, it only returns any which are applicable or the default, or it returns no answer.
So geolocation is ideal if you want to restrict content—for example, providing content for the US market only. If you want to do that, then you can create a US record and only people located in the US will receive that record as a response for any queries. You can also use this policy type to provide language specific content or to load balance across regional endpoints based on customer location.
Now one last time, because this is really important for the exam and for real world usage: this routing policy type is not about the closest record—geolocation returns relevant locations only. You will not get a Canadian record returned if you're based in the UK and no closer records exist. The smallest type of record is a subdivision which is a US state, then you have country, then you have continent, and finally optionally a default record. Use the geolocation routing policy if you want to route traffic based on the location of your customers.
Now it's important that you understand—which is why I've stressed this so much—that geolocation isn't about proximity, it's about location. You only have records returned if the location is relevant. So if you're based in the US but are based in a different state than a record, you won't get that record. If you're based in the US and there is a record which is tagged as the US as a country, then you will get that record returned. If there isn't a country specific record but there is one for the continent that you're in, you'll get that record returned, and then the default is a catchall. It's optional; if you choose to add it, then it's returned if your user is in a location where you don't have a specific record tagged to that location.
Now that's everything that I wanted to cover in this video. Thanks for watching. Go ahead and complete the video and when you're ready I look forward to you joining me in the next.
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blog.joewoods.dev blog.joewoods.dev
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Joe Wood keeps a 'vague' list of tasks that are equally important as other more tangible tasks but lack clarity about what steps to take. He added this within his GTD implementation. Interesting, as I notice I tend to put off important things when I don't have a clear path to execution yet (and the next action would be to think about those steps). I also think such vague actions may actually not be actions but projects lacking definition. It makes beginning harder, and keeping a vague list might help address it. I think I might use it as a tag in tasks, not as a separate list.
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www.youtube.com www.youtube.com
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Briefing Document : Le Refus Scolaire Anxieux
Source : Excerpts de la transcription de la conférence "Le refus scolaire anxieux : mieux le reconnaitre, mieux le comprendre pour mieux le soigner" avec le Docteur Hélène Denis, pédopsychiatre au CHU de Montpellier.
Date de la conférence : 2025
Thèmes Principaux :
Définition et distinction du Refus Scolaire Anxieux (RSA) :
Le Dr. Denis insiste sur l'importance d'utiliser le terme "refus scolaire anxieux" plutôt que "phobie scolaire", qu'elle considère comme un terme obsolète et imprécis.
Le RSA est défini comme l'incapacité pour un enfant ou un adolescent d'aller à l'école en raison d'une anxiété intense.
Elle cite la définition de Juria Guérin (1974) : enfants ou adolescents qui, pour des raisons irrationnelles, refusent d'aller à l'école et résistent avec des réactions d'anxiété vive ou de panique à l'idée d'y aller, malgré les efforts pour les y forcer.
- "le refus scolaire anxieux qu'est-ce que c'est et ben c'est ce qu'on appelle dans le jargon populaire la phobie scolaire et il faut plus employer ce mot-là à partir de ce soir phobie scolaire ça veut plus trop rien dire"
- "ce sont des enfants ou des adolescents qui n'arrivent plus à aller à l'école parce qu'ils sont anxieux et que cette anxiété est tellement forte qu'il n'arrive plus à y aller"
- Caractéristiques des jeunes souffrant de RSA : Contrairement à l'absentéisme scolaire classique (école buissonnière), les jeunes atteints de RSA veulent retourner à l'école, ont des ambitions scolaires et souffrent de cette situation. Ils sont souvent conscients du caractère irrationnel de leurs peurs anxieuses et demandent de l'aide.
- "la particularité de ces jeunes qui ne qui sont absents parce qu'il n'arrivent plus à aller à l'école pour des raisons anxieux sont des patients qui veulent retourner à l'école ils ont des ambitions scolaires ils étaient auparavant plutôt très intéressés voir très investis dans la scolarité et à un moment donné ils n'arrivent plus à y aller et ce sont des jeunes qui du coup souffrent de cette situation et demandent de l'aide"
Le RSA comme complication de troubles anxieux : Le RSA n'est pas un diagnostic en soi dans les classifications internationales, mais plutôt une manifestation ou une complication de troubles anxieux sous-jacents (un ou plusieurs).
Le Dr. Denis présente les critères de Berg pour définir les patients concernés par le RSA dans le cadre de la recherche : refus d'aller à l'école entraînant une absence prolongée, détresse émotionnelle anticipatoire (peur, colère, tristesse, symptômes physiques), maintien au domicile pendant les heures de classe, absence de comportements antisociaux significatifs et efforts parentaux préalables pour la rescolarisation.
"le refus scolaire anxieux c'est pas un diagnostic qui est dans les classifications parce qu'en fait c'est une complication de plusieurs troubles anxieux"
Les Troubles Anxieux : Le Dr. Denis souligne la sous-reconnaissance et la mauvaise prise en charge des troubles anxieux en France.
Elle explique que l'anxiété est une émotion normale et utile, mais que les troubles anxieux se caractérisent par une peur exagérée, intense, fréquente et durable, entraînant une souffrance importante et des comportements d'évitement.
Elle détaille différents types de troubles anxieux chez l'enfant et l'adolescent : anxiété de séparation, phobies spécifiques, trouble anxiété généralisée (TAG), anxiété sociale (y compris l'anxiété de performance), trouble panique et troubles obsessionnels compulsifs (TOC) (bien que n'étant plus classés comme troubles anxieux, ils peuvent entraîner un RSA).
- "les troubles anxieux c'est une c'est une pathologie qui est très peu connue ou très mal diagnostiquée et très très mal prise en charge en France"
- "les troubles anxieux c'est une peur normale qui va être très exagérée au départ ça peut être une peur normale mais on n'arrive pas à trouver la résolution ou alors c'est une peur normale qui a trouvé une résolution qui revient très forte à un autre moment du développement"
Conséquences des Troubles Anxieux non traités : Le Dr. Denis insiste sur les répercussions importantes des troubles anxieux non traités sur le développement psychologique, la vie familiale, les apprentissages scolaires, et le risque accru de développer à l'âge adulte des troubles anxieux persistants, une dépression, ou des conduites addictives (abus de substances pour gérer l'anxiété).
"le problème des troubles anxieux de l'enfant et de l'adolescent c'est que si on n'y fait rien il y a pas de raison que ça s'arrête et donc on va laisser se construire comme ça un adulte anxieux sans s'en être occupé sans avoir arrêté cette trajectoire d'anxiété"
Diagnostic Différentiel du RSA : Il est crucial de distinguer le RSA de l'absentéisme scolaire volontaire (école buissonnière), qui n'est pas motivé par l'anxiété et où les jeunes n'expriment pas de souffrance ni de désir de retourner à l'école. La distinction peut parfois être complexe, notamment en présence de facteurs familiaux compliqués.
"ce qui n'est pas un refus scolaire anxieux c'est ceux qui ne vont pas à l'école mais parce qu'ils n'ont pas envie d'y aller ce sont des jeunes qu'on appelle école buissonnière"
Traitement du RSA : Le traitement de référence, basé sur les études internationales, est la Thérapie Cognitive et Comportementale (TCC), éventuellement associée à un traitement médicamenteux (antidépresseurs ISRS).
La TCC vise à apprendre au patient à identifier et à modifier ses pensées dysfonctionnelles, à gérer ses émotions et à s'exposer progressivement aux situations anxiogènes.
"dans les études scientifiques de bonne qualité on retrouve qu'il faut faire de la thérapie cognitive et comportementale qui est le traitement de référence des troubles anxieux"
"la technique de référence c'est s'exposer aux situations qui font peur on va préparer le patient doucement mais sûrement à s'exposer à ce qui fait peur"
Prise en charge spécifique au CHU de Montpellier : L'unité du Dr. Denis propose une prise en charge spécifique en hospitalisation de jour pour les adolescents (11-16 ans) souffrant de RSA.
Cette prise en charge combine scolarité adaptée au sein de l'unité avec des thérapies cognitives et comportementales individuelles et en groupe.
Un travail important est mené en partenariat avec les familles et les établissements scolaires pour faciliter le retour à l'école.
"l'unité du docteur Hélène Denis au CHU de Montpellier a développé une prise en charge spécifique ces patients qui ont en général entre 11 et 16 ans [...] sont reçus en hospitalisation de jours durant cette période ils poursuivent leurs études au sein de l'unité et reçoivent des soins en thérapie cognitive et comportementale à la fois en individuel et en groupe"
Rôle de l'Éducation Nationale dans la détection et la prise en charge précoce : Le Dr. Denis encourage les professionnels de l'éducation à être attentifs aux signes d'anxiété liés à la scolarité (peur exprimée, somatisations, absences perlées), à adopter une attitude empathique et bienveillante, à proposer des aménagements scolaires si nécessaire (temps partiel), à faciliter la verbalisation des peurs, et à orienter vers une aide spécialisée en cas de persistance ou d'aggravation. Elle souligne l'importance du lien avec les parents.
"aller chercher avec des mots simples et une reconnaissance empathique et bienveillante de 'Mais qu'est-ce qui te fait peur ? même si c'est débile tu peux peut-être me le dire'"
"il vaut mieux aménager faire du temps partiel plutôt que s'acharner et après tout bloquer la déscolarisation totale c'est l'enfer pour repartir c'est l'enfer il vaut mieux y rester un peu et moins souvent et et mettre en place des stratégies pour essayer que petit à petit on y reparte"
Points de vigilance : Le Dr. Denis exprime un regard critique sur certaines approches et terminologies dans le domaine de l'éducation, notamment concernant le "haut potentiel intellectuel" (HPI), qu'elle considère comme une invention franco-française problématique et non étayée scientifiquement comme cause de mal-être scolaire.
Elle met également en garde contre une utilisation excessive et parfois inappropriée du terme "harcèlement". Idées ou Faits Importants :
- Le refus scolaire anxieux est une problématique fréquente et invalidante chez les adolescents.
- Il est essentiel de distinguer le RSA de l'absentéisme non anxieux pour une prise en charge adaptée.
- Les troubles anxieux sous-jacents sont souvent mal diagnostiqués et pris en charge en France.
- La TCC est le traitement de référence du RSA et des troubles anxieux.
- Une prise en charge multidisciplinaire et un partenariat étroit avec les familles et les écoles sont cruciaux pour un retour à l'école réussi.
- La détection précoce et les aménagements scolaires peuvent prévenir une déscolarisation totale.
- Certaines notions populaires comme le lien systématique entre HPI et mal-être scolaire sont remises en question par le Dr. Denis.
Conclusion :
La conférence du Dr. Hélène Denis met en lumière la complexité du refus scolaire anxieux, son lien étroit avec les troubles anxieux, et l'importance d'une approche diagnostique et thérapeutique rigoureuse.
Elle souligne le rôle crucial des professionnels de l'éducation dans la détection précoce et l'orientation, ainsi que la nécessité d'une collaboration étroite avec les équipes médicales et les familles pour accompagner au mieux ces jeunes en souffrance et favoriser leur retour à l'école.
La présentation du dispositif spécifique du CHU de Montpellier offre un exemple concret de prise en charge efficace basée sur la TCC.
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Author response:
The following is the authors’ response to the original reviews
Public Reviews:
Reviewer #1 (Public Review):
Astrocytes are known to express neuroligins 1-3. Within neurons, these cell adhesion molecules perform important roles in synapse formation and function. Within astrocytes, a significant role for neuroligin 2 in determining excitatory synapse formation and astrocyte morphology was shown in 2017. However, there has been no assessment of what happens to synapses or astrocyte morphology when all three major forms of neuroligins within astrocytes (isoforms 1-3) are deleted using a well characterized, astrocyte specific, and inducible cre line. By using such selective mouse genetic methods, the authors here show that astrocytic neuroligin 1-3 expression in astrocytes is not consequential for synapse function or for astrocyte morphology. They reach these conclusions with careful experiments employing quantitative western blot analyses, imaging and electrophysiology. They also characterize the specificity of the cre line they used. Overall, this is a very clear and strong paper that is supported by rigorous experiments. The discussion considers the findings carefully in relation to past work. This paper is of high importance, because it now raises the fundamental question of exactly what neuroligins 1-3 are actually doing in astrocytes. In addition, it enriches our understanding of the mechanisms by which astrocytes participate in synapse formation and function. The paper is very clear, well written and well illustrated with raw and average data.
We thank the reviewer for the balanced and informative summary.
Reviewer #2 (Public Review):
In the present manuscript, Golf et al. investigate the consequences of astrocyte-specific deletion of Neuroligin family cell adhesion proteins on synapse structure and function in the brain. Decades of prior research had shown that Neuroligins mediate their effects at synapses through their role in the postsynaptic compartment of neurons and their transsynaptic interaction with presynaptic Neurexins. More recently, it was proposed for the first time that Neuroligins expressed by astrocytes can also bind to presynaptic Neurexins to regulate synaptogenesis (Stogsdill et al. 2017, Nature). However, several aspects of the model proposed by Stogsdill et al. on astrocytic Neuroligin function conflict with prior evidence on the role of Neuroligins at synapses, prompting Golf et al. to further investigate astrocytic Neuroligin function in the current study. Using postnatal conditional deletion of Neuroligins 1, 2 and 3 specifically from astrocytes, Golf et al. show that virtually no changes in the expression of synaptic proteins or in the properties of synaptic transmission at either excitatory or inhibitory synapses are observed. Moreover, no alterations in the morphology of astrocytes themselves were found. The authors conclude that while Neuroligins are indeed expressed in astrocytes and are hence likely to play some role there, this role does not include any direct consequences on synaptic structure and function, in direct contrast to the model proposed by Stogsdill et al.
Overall, this is a strong study that addresses an important and highly relevant question in the field of synaptic neuroscience. Neuroligins are not only key regulators of synaptic function, they have also been linked to numerous psychiatric and neurodevelopmental disorders, highlighting the need to precisely define their mechanisms of action. The authors take a wide range of approaches to convincingly demonstrate that under their experimental conditions, no alterations in the levels of synaptic proteins or in synaptic transmission at excitatory or inhibitory synapses, or in the morphology of astrocytes, are observed.
We are also grateful for this reviewer’s constructive comments.
One caveat to this study is that the authors do not directly provide evidence that their Tamoxifen-inducible conditional deletion paradigm does indeed result in efficient deletion of all three Neuroligins from astrocytes. Using a Cre-dependent tdTomato reporter line, they show that tdTomato expression is efficiently induced by the current paradigm, and they refer to a prior study showing efficient deletion of Neuroligins from neurons using the same conditional Nlgn1-3 mouse lines but a different Cre driver strategy. However, neither of these approaches directly provide evidence that all three Neuroligins are indeed deleted from astrocytes in the current study. In contrast, Stogsdill et al. employed FACS and qPCR to directly quantify the loss of Nlgn2 mRNA from astrocytes. This leaves the current Golf et al. study somewhat vulnerable to the criticism, however unlikely, that their lack of synaptic effects may be a consequence of incomplete Neuroligin deletion, rather than a true lack of effect of astrocytic Neuroligins.
The concern is valid. In the original submission of this paper, we did not establish that the Cre recombinase we used actually deleted neuroligins in astrocytes. We have now addressed this issue in the revised paper with new experiments as described below.
However, the reviewer’s impression that the Stogsdill et al. paper confirmed full deletion of Nlgn2 is a misunderstanding of the data in that paper. The reviewer is correct that Stogsdill et al. performed FACS to test the efficacy of the GLAST-Cre mediated deletion of Nlgn2-flox mice, followed by qRT-PCR comparing heterozygous with homozygous mutant mice. With their approach, no wild-type control could be used, as these would lack reporter expression. However, this experiment does NOT allow conclusions about the degree of recombination, both overall recombination (i.e. recombination in all astrocytes regardless of TdT+) and recombination in TdT+ astrocytes because it doesn’t quantify recombination. To quantify the degree of recombination, the paper would have had to perform genomic PCR measurements.
The problem with the data on the degree of recombination in the Stogsdill et al. (2017) paper, as we understand them, is two-fold.
First, the GLAST-Cre line only targets ~40-70% of astrocytes, at least as evidenced by highly sensitive Cre-reporter mice in a variety of studies using this Cre line. The 40-70% variation is likely due to differences in the reporter mice and the tamoxifen injection schedule used. In comparison, we are targeting most astrocytes using the Aldh1l1-CreERT2 mice. Moreover, GLAST-Cre mice exhibit neuronal off-targeting, consistent with at least some of the remaining Nlgn2 qRT-PCR signal in the FACS-sorted cells. As we describe next, this signal also likely comes from astrocytes where recombination was incomplete This is the reason why we, like everyone else, are now using the Aldh1l1-Cre line that has been shown to be more efficient both in terms of the overall targeting of astrocytes (i.e. nearly complete) and the level of recombination observed in reporter(+) astrocytes.
Second, Stogsdill et al. detected a significant decrease in the Nlgn2 qRT-PCR signal in the FACS-sorted homozygous Nlgn2 KO cells compared to the heterozygous Nlgn2 KO cells but the Nlgn2 qRT-PCR signal was still quite large. The data is presented as normalized to the HET condition. As a result, we don’t know the true level of gene deletion (i.e. compared to TdT- astrocytes). For example, based on the Stogsdill et al. data the HET manipulation could have induced only a 20% reduction in Nlgn2 mRNA levels in TdT(+) astrocytes, in which case the KO would have produced a 40% reduction in Nlgn2 mRNA in TdT(+) astrocytes. Moreover, it is possible based on our own experience with the GLAST-Cre line, that the reporter may also not turn on in some astrocytes where other alleles have been independently recombined – just as some astrocytes that are Td(+) would still be wild-type or heterozygous for Nlgn2. Thus, it is impossible to calculate the actual percentage of recombination from these data, even in TdT(+) cells, absent of PCR of genomic DNA from isolated cells. Alternatively, comparison of mRNA levels using primers sensitive to floxed sequences in wild-type controls versus cKO mice would have also yielded a much better idea of the recombination efficiency.
In summary, it is unclear whether the Nlgn2 deletion in the Stogsdill et al. paper was substantial or marginal – it is simply impossible to tell.
Reviewer #3 (Public Review):
This study investigates the roles of astrocytes in the regulation of synapse development and astrocyte morphology using conditional KO mice carrying mutations of three neuroligins1-3 in astrocytes with the deletion starting at two different time points (P1 and P10/11). The authors use morphological, electrophysiological, and cell-biological approaches and find that there are no differences in synapse formation and astrocyte cytoarchitecture in the mutant hippocampus and visual cortex. These results differ from the previous results (Stogsdill et al., 2017), although the authors make several discussion points on how the differences could have been induced. This study provides important information on how astrocytes and neurons interact with each other to coordinate neural development and function. The experiments were well-designed, and the data are of high quality.
We also thank this reviewer for helpful comments!
Recommendations for the authors:
This project was meant to rigorously test the intriguing overall question whether neuroligins, which are abundantly expressed in astrocytes, regulate synapse formation as astrocytic synapse organizers. The goal of the paper was NOT to confirm or dispute the conclusion by Stogsdill et al. (Nature 2017) that Nlgn2 expressed in astrocytes is essential for excitatory synapse formation and that astrocytic Nlgn1-3 are required for proper astrocyte morphogenesis. Instead, the project was meant to address the much broader question whether the abundant expression of any neuroligin, not just Nlgn2, in astrocytes is essential for neuronal excitatory or inhibitory synapse formation and/or for the astrocyte cytoarchitecture. We felt that this was an important question independent of the Stogsdill et al. paper. We analyzed in our experiments young adult mice, a timepoint that was chosen deliberately to avoid the possibility of observing a possible developmental delay rather than a fundamental function that extends beyond development.
We do recognize that the conclusion by Stogsdill et al. (2017) that Nlgn2 expression in astrocytes is essential for excitatory synapse formation was very exciting to the field but contradicted a large literature demonstrating that Nlgn2 protein is exclusively localized to inhibitory synapses and absent from excitatory synapses (to name just a few papers, see Graf et al., Cell 2004; Varoqueaux et al., Eur. J. Cell Biol. 2004; Patrizi et al., PNAS 2008; Hoon et al., J. Neurosci. 2009). In addition, the conclusion of Stogsdill et al. that astrocytic Nlgn2 specifically drove excitatory synapse formation was at odds with previous findings documenting that the constitutive deletion of Nlgn2 in all cells, including astrocytes, has no effect on excitatory synapse numbers (again, to name a few papers, see Varoqueaux et al., Neuron 2006; Blundell et al., Genes Brain Behav. 2008; Poulopoulos et al., Neuron 2009; Gibson et al., J. Neurosci. 2009). These contradictions conferred further urgency to our project, but please note that this project was primarily driven by our curiosity about the function of astrocytic neuroligins, not by a fruitless desire to test the validity of one particular Nature paper.
The general goal of our paper notwithstanding, few papers from our lab have received as much attention and as many negative comments on social media as this paper when it was published as a preprint. Because we take these criticisms seriously, we have over the last year performed extensive additional experiments to ensure that our findings are well founded. We feel that, on balance, our data are incompatible with the notion that astrocytic neuroligins play a fundamental role in excitatory synapse formation but are consistent with other prior findings obtained with neuroligin KO mice. In the new data we added to the paper, we not only characterized the Cre-mediated deletion of neuroligins in depth, but also employed an independent second system -human neurons cultured on mouse glia- to further validate our conclusions as described below. Although we believe that our results are incompatible with the notion that astrocytic neuroligins fundamentally regulate excitatory or inhibitory synapse formation, we also conclude with regret that we still don’t know what astrocytic neuroligins actually do. Thus, the function of astrocytic neuroligins, as there surely must be one, remains a mystery.
Finally, there are many possible explanations for the discrepancies between our conclusions and those of Stogsdill et al. as described in our paper. Most of these explanations are technical and may explain why not only our, but also the results of many other previous studies from multiple labs, are inconsistent with the conclusions by Stogsdill et al. (2017), as discussed in detail in the revised paper.
Reviewer #1 (Recommendations For The Authors):
The paper is very clear and well written. I have only one comment and that is to increase the sizes of Figs 2, 4 and 6 so that the imaging panels can be seen more clearly. Also, although I know the n numbers are provided in the figure legends, the authors may help the reader by providing them in the results when key data and findings are reported.
We agree and have followed the reviewer’s suggestions as best as we could.
Reviewer #2 (Recommendations For The Authors):
(1) Given the strength and importance of the claims that the authors make, I would highly recommend adding some quantitative evidence regarding the efficacy of deletion in astrocytes, e.g. using the same strategy as in Stogsdill et al. As unlikely as it may be that Neuroligin deletion is in fact incomplete, this possibility cannot be excluded unless directly measured. To avoid future discussions on this subject, it seems that the onus is on the authors to provide this information.
We concur that this is an important point and have devoted a year-long effort to address it. Note, however, that the strategy employed by Stogsdill et al. does not actually allow conclusions about their recombination efficiency. As described above, it only allows the conclusion that some recombination took place. The Stogsdill et al. Nature paper (2017) is a bit confusing on this point. This approach is thus not appropriate to address the question raised by the reviewer.
We have performed two experiments to address the issue raised by the reviewer.
First, we used a viral (i.e. AAV2/5) approach to express Rpl22 with a triple HA-tag, also known as Ribotag, which allows us to purify ribosome-bound mRNA from targeted cells for downstream gene expression analysis. The novel construct is driven by the GfaABC1D promoter and includes two additional features which make it particularly useful. First, upstream of Ribotag is a membrane-targeted, Lck-mVenus followed by a self-cleaving P2A sequence. This allows easy visualization of targeted astrocytes. Second, we have incorporated a cassette of four copies of six miRNA targeting sequences (4x6T) for mIR-124 as was recently published (Gleichman et al., 2023) to eliminate off-target expression in neurons. Based on qPCR analysis, the updated construct allowed >95% de-enrichment of neuronal mRNA and slightly improved observed recombination rates (~10% per gene) relative to an earlier version without 4x6T. Mice that were injected with tamoxifen at P1, similar to other experiments in the paper, were then stereotactically injected at ~P35-40 within the dorsal hippocampus with AAV2/5-GfaABC1D-Lck-mVenus-P2A-Rpl22-HA-4x6T. Approximately 3 weeks later, acute slices were prepared, visualized for fluorescence, and both CA1 and nearby cortex that was partially targeted were isolated for downstream ribosome affinity purification with HA antibodies. Total RNA was saved as input. qPCR was performed using assays that are sensitive to the exons that are floxed in the Nlgn123 cKO mice, so that our quantifications are not confounded by potential differences in non-sense mediated decay. Our control data reveals a striking enrichment of an astrocyte marker gene (e.g. aquaporin-4) and de-enrichment of genes for other cell types. In the CA1, we observed robust loss of Nlgn3 (~96%), Nlgn2 (~86%), and Nlgn1 (65%) gene expression. Similarly, in the cortex, we observed a similarly robust loss of Nlgn3 (93%), Nlgn2 (83%), and Nlgn1 (72%) expression. Given that our targeting of astrocytes based on Ai14 Cre-reporter mice was ~90-99%, these reductions are striking and definitive. The existence of some residual transcript reflects the presence of a small population of astrocytes heterozygous for Nlgn2 and Nlgn3. In contrast, Nlgn1 appears more difficult to recombine and it is likely that some astrocytes are either heterozygous or homozygous knockout cells. Although it is thus possible that Nlgn1 could provide some compensation in our experiments, it is worth noting that Stogsdill et al. found that only Nlgn2 and Nlgn3 knockdown with shRNAs resulted in impaired astrocyte morphology by P21. Moreover, they found that Nlgn2 cKO in astrocytes with PALE of a Cre-containing pDNA impaired astrocyte morphology in a gene-dosage dependent manner and suppressed excitatory synapse formation at P21. Thus, our inability to delete all of Nlgn1 doesn’t readily explain contradictions between our findings and theirs.
Second, in an independent approach we have cultured glia from mouse quadruple conditional Nlgn1234 KO mice and infected the glia with lentiviruses expressing inactive (DCre, control) or active Cre-recombinase. We confirmed complete recombination by PCR. We then cultured human neurons forming excitatory synapses on the glia expressing or lacking neuroligins and measured the frequency and amplitude of mEPSCs as a proxy for synapse numbers and synaptic function. As shown in the new Figure 9, we detected no significant changes in mEPSCs, demonstrating in this independent system that the glial neuroligins do not detectably influence excitatory synapse formation.
(2) Along the same lines, the authors should be careful not to overstate their findings in this direction. For example, the figure caption for Figure 2 reads 'Nlgn1-3 are efficiently and selectively deleted in astrocytes by crossing triple Nlgn1-3 conditional KO mice with Adh1l1-CreERT2 driver mice and inducing Cre-activity with tamoxifen early during postnatal development'. This is not technically correct and should be modified to reflect that the authors are not in fact assessing deletion of Nlgn1-3, but only expression of a tdTomato reporter.
We agree – this is essentially the same criticism as comment #1.
(3) In general, the animal numbers used for the experiments are rather low. With an n = 4 for most experiments, only large abnormalities would be detected anyway, while smaller alterations would not reach statistical significance due to the inherent biological and technical variance. For the most part, this is not a concern, since there really is no difference between WTs and Nlgn1-3 cKOs. However, trends are observed in some cases, and it is conceivable that these would become significant changes with larger n's, e.g. Figure 3H (Vglut2); Figure 4E (VGlut2 S.P., D.G.); Figure 6D (Vglut2). Increasing the numbers to n = 6 here would greatly strengthen the claims that no differences are observed.
We concur that small differences would not have been detected in our experiments but feel that given the very large phenotypes of the neuroligin deletions in neurons and of the phenotypes reported by Stogsdill et al. (2017), which also did not employ a large number of animals, a very small phenotype in astrocytes would not have been very informative.
Minor points:
(1) Please state the exact genetic background for the mouse lines used.
Our lab generally uses hybrid CD1/Bl6 mice to avoid artifacts produced by inbred genetic mutations in so-called ‘pure’ lines, especially Bl6 mice. This standard protocol was followed in the present study. Thus, the mice are on a mixed CD1/Bl6 hybrid background.
Reviewer #3 (Recommendations For The Authors):
(1) Figure 4 demonstrates that neuroligin 1-3 deletions restricted to astrocytes do not affect the number of excitatory and inhibitory synapses in layer IV of the primary visual cortex. This conclusion could be further strengthened if the authors could provide electrophysiological evidence such as mE/IPSCs.
We agree but have chosen a different avenue to further test our conclusions because slice electrophysiological experiments are time-consuming, labor intensive, and difficult to quantitate, especially in cortex.
Specifically, we have co-cultured human neurons with astrocytes that either contain or lack neuroligins (new Fig. 9). With this experimental design, we have total control over ALL neuroligins in astrocytes. Electrophysiological recordings then demonstrated that the complete deletion of all glial neuroligins has no effect on mEPSC frequencies and amplitudes. Although clearly much more needs to be done, the new results confirm in an independent system that glial neuroligins have no effect on synapse formation in the neurons, even though neurons depend on astrocytes for synaptogenic factors as Ben Barres brilliantly showed a decade ago. However, it is important to note that dissociated glia in culture, while synaptogenic, are reactive and may not faithfully recapitulate all roles of astrocytes in synaptogenesis.
(2) It would help readers if the images showing the punctate double marker stainings of excitatory/inhibitory synapses are presented in merged colors (i.e., yellow colors for red and green puncta colors).
We have tried to improve the visualization of the rather voluminous studies we performed and illustrate in the figures as best as we could.
(3) The resolutions of the images in the figures are not good, although I guess it is because the images are for review processes.
We apologize and would like to assure the reviewer that we are supplying high-resolution images to the journal.
(4) Typos in lines 82 and 274.
We have corrected these errors.
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Reply to the reviewers
Manuscript number: RC- 2025-02880
Corresponding author(s): Monica, Gotta
1. General Statements [optional]
We thank the reviewers for their useful comments that will improve our manuscript and make it clearer. We agree with Reviewer 1 that SDS-22 has more general functions in cellular processes by maintaining GSP-1/-2 levels, rather than only regulating cell polarity. We have now modified our conclusion in the text (all changes are highlighted in yellow) and we hope that it is now more clear and better explained. Below we address the reviewer’s comments one by one and indicate how we have or will address the comments in the final version. We expect the revisions to take 2-3 months.
2. Description of the planned revisions
Major comments
Reviewer 1
(1) Overall, the evidence supporting the core finding that SDS-22 is required for normal GSP-1/2 levels is strong and well documented. The experiments were performed well and controls, statistics, replicates were appropriate. Our only slight reservation was whether the effect of sds-22(RNAi) on stability may be overstated due to the use of GFP fusions to GSP-1/2 for this analysis. The authors note these alleles are hypomorphic, potentially raising the possibility that GFP tags destabilise the proteins and make them more prone to degradation. Ideally this would be repeated with an untagged allele via Western (e.g. Peel et al 2017 for relevant antibodies).
We thank the reviewer for the general comments. To address this important point on the protein levels we have requested GSP-1 and GSP-2 antibodies reported in Peel et al and Tzur et al (Peel et al, 2017; Tzur et al, 2012). The published GSP-1 antibody has been used in western blot, and the GSP-2 antibody has been used in both immunostaining and Western blot analysis. Despite our efforts, we were not able to detect GSP-2 neither on western blots nor on immunostainings with the aliquot we have received. On the opposite, GSP-1 antibodies worked well on western blot. We have already measured the GSP-1 levels in SDS-22 depleted embryos (N=2, see below) and we observed reduced levels, confirming our initial result. However, as the reviewer rightly pointed out, the levels are reduced by 20% (rather than about 50% as in the GFP strain), suggesting that indeed the GFP fusion does contribute to the instability. We will measure GSP-1 levels in at least an additional sds-22(RNAi) experiment and in sds-22(E153A) embryos.
Left, Western Blot of embryonic extracts from N2 in ctrl(RNAi) and sds-22(RNAi) embryos. Tubulin is used as a loading control. Right, Fold change of GSP-1 normalized to Tubulin levels. N = 2.
Since we could not detect endogenous GSP-2 with the antibodies we have received, we will generate an OLLAS-tagged GSP-2 strain. OLLAS is a commonly used tag consisting of 14 amino acids (Park et al, 2008), with an additional 4 amino acids as a linker. The tag is much smaller than mNeonGreen, which consists of approximately 270 amino acids. We will then measure the GSP-2 levels using the ollas antibody in sds-22(RNAi) embryos. We will also cross this strain with sds-22(E153A) and measure OLLAS::GSP-2 levels in this mutant. If this strain is not embryonic lethal, as in the case of the mNG::gsp-2; sds-22(E153A) (Fig EV6A), it will also suggest that ollas::gsp-2 does not behave as hypomorph.
These data will complement the data shown in Fig 6.
(2) The role for SDS-22 in polarity is rather weak. Both the SDS-22 depletion phenotypes and the ability of SDS-22 depletion to suppress pkc-3(ts) polarity phenotypes are modest (and weaker in than GSP-2 depletion). For example, the images in Figure 1B appear striking, but from Movie S1 it is clear that this isn't a full rescue as PAR-2 is initially uniformly enriched on the cortex (rather than mostly cytoplasmic) and it is never fully cleared. In the movie, the clearance at the point of pronuclear meeting is very modest. Quantitation might be helpful here (i.e. as in Figure 3G). As the authors state, it seems that SDS-22 does not have a specific role in polarity beyond the general effect on GSP-1/2 levels. This does not undermine the core message of the paper, but we would recommend downplaying the conclusions with respect to contributing to polarity establishment. For example "...suggesting that SDS-22 regulates GSP-1/-2 activity to control the loading of PAR-2 to the posterior cortex in one-cell stage C. elegans embryos" implies a regulatory role for SDS-22 in polarity, but we would interpret it as simply helping reduce aberrant degradation of GSP-1/2 and this impacts a variety of cellular processes including polarity.
We agree with the reviewer that the rescue of pkc-3ts polarity defects by SDS-22 depletion is not as strong as GSP-2 depletion, and as suggested, we have re-quantified the phenotype, as we did in Fig 3G, as shown below in Fig 1C.
This has replaced Fig.1 in the manuscript.
Accordingly, we have clarified this in the text in several locations. We have added “partial” rescue in many places and modified conclusions in the results and discussion. The changes are all highlighted and the major ones are also below:
From Result Line 119-121, page 5:
“In contrast, depletion of SDS-22 resulted in PAR-2 localization being restricted to the posterior cortex in 87.5% of the one-cell stage embryos (Fig 1B) and PAR-2 was localized to the P1 blastomere after the first cell-division (Movie EV1).”
To: Result Line 122-125, page 5
“In contrast, depletion of SDS-22 resulted in PAR-2 localization being enriched in the posterior cortex in 87.5% of the one-cell stage embryos (Fig 1B,C) and PAR-2 was localized to the P1 blastomere after the first cell-division (Movie EV1).”
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From Result Line 172-175, page 7:
“Our data show that depletion of SDS-22 results in a smaller PAR-2 domain, suppresses the polarity defects of a pkc-3 temperature sensitive strain and the aberrant PAR-2 localization observed in the PAR-2(L165V) mutant strain. As SDS-22 is a conserved PP1 regulator, our data suggest that SDS-22 positively regulates GSP-2 in polarity establishment.”
To: Result Line 178-181, page 7
“Our data show that depletion of SDS-22 results in a smaller PAR-2 domain, partially suppresses the polarity defects of a pkc-3 temperature sensitive strain and the aberrant PAR-2 localization observed in the PAR-2(L165V) mutant strain. As SDS-22 is a conserved PP1 regulator, our data suggest that SDS-22 positively regulates GSP-2.”
From Result Line 256-257, page 10:
“suggesting that the interaction of SDS-22 with the PP1 phosphatases is important for polarity establishment.”
To: Result Line 264-265, page 10
“suggesting that the interaction of SDS-22 with the PP1 phosphatases contributes to polarity establishment”
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From Result Line 311-313, page 12:
To conclude, while our genetic data on PAR-2 cortical localization suggest that SDS-22 is not required to fully activate GSP-1 and/or GSP-2, depletion or mutation of SDS-22 results in a reduced activity of the phosphatases.
To: Result Line 319-322, page 12
To conclude, while our genetic data on PAR-2 cortical localization suggest that SDS-22 is not required to fully activate GSP-1 and/or GSP-2, depletion or mutation of SDS-22 results in a reduced activity of the phosphatases, as shown by phospho-histone H3 (Ser10) levels. This suggests that SDS-22 plays a general role in regulating GSP-1 and GSP-2, which is not specific to cell polarity.
From Result Line 391-392, page 15:
In summary, our results show that SDS-22 maintains the levels of GSP-1 and GSP-2 by protecting them
392 from proteasome mediated degradation.
To: Result Line 402-403, page 15
In summary, these data show that SDS-22 is important to maintain the levels of GSP-1 and GSP-2 by protecting them from proteasome mediated degradation.
We have also rephrased our conclusion according to Reviewer 1’s suggestion.
From Introduction Line 95-101, Page 4:
Here we show that SDS-22 depletion rescues the polarity defects caused by reduced PAR-2 phosphorylation in the pkc-3(ne4246) mutant at the semi-restrictive temperature (24°C), similarly to the depletion of GSP-2. Depletion of SDS-22 results in lower GSP-1 and GSP-2 protein levels which can be rescued by depleting proteasomal subunits. These results establish SDS-22 as a regulator of PAR polarity establishment in the C. elegans one-cell embryo and are consistent with and complement the recent data in mammalian cells showing that SDS22 is important to control the stability of the PP1 phosphatase (Cao et al., 2024).
To: Introduction Line 96-101, Page 4
*Here we show that SDS-22 depletion partially rescues the polarity defects caused by reduced PAR-2 phosphorylation in the pkc-3(ne4246) mutant at the semi-restrictive temperature (24°C). Depletion of SDS-22 results in lower GSP-1 and GSP-2 protein levels which can be rescued by depleting proteasomal subunits. These results establish that SDS-22 contributes to cell polarity by regulating GSP-1/-2 levels and are consistent with and complement the recent data in mammalian cells showing that SDS22 is important to control the stability of the PP1 phosphatase (Cao et al., 2024). *
From Discussion Line 417-420, page 17:
Depletion of SDS-22, or mutation of its E153 residue (E153A) important for SDS-22-PP1 interaction resulted in reduced GSP-1/-2 protein levels, decreased dephosphorylation of a PP1 substrate, and a smaller PAR-2 domain, suggesting that SDS-22 regulates GSP-1/-2 activity to control the loading of PAR-2 to the posterior cortex in one-cell stage C. elegans embryos.
To: Discussion Line 426-429, page 17
*Here we find that a conserved PP1 regulator, SDS-22, when depleted, results in a smaller PAR-2 domain and can partially rescue the polarity defects of a pkc-3(ne4246) mutant. We demonstrate that SDS-22 contributes to the activity of GSP-1/-2 by protecting them from proteasomal degradation and maintaining their protein levels. *
Add new discussion to Discussion Line 429-432, page 17:
Taken together, our data suggest that the role of SDS-22 in polarity is indirect via the regulation of GSP-1/-2 levels. In support of this, SDS-22 depletion results in broader GSP-1/-2 dependent phenotypes such as increased Phospho-H3 (Ser10) (Fig 5) and centriole duplication defects in later-stage embryos (Peel et al., 2017).
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(3) Specificity of SDS-22 effects on polarity. SDS-22 (or GSP-1/2) depletion is likely to have effects on many pathways. We wondered whether some of the polarity phenotypes may not be specifically due to changes in the PAR-2 phosphorylation cycle as implied.
One candidate is the actomyosin cortex. It was noticeable that control and sds-22 embryos were different: In Movies S1, S2, and S3 control embryos show either stronger or more persistent cortical ruffling or pseudocleavage furrows. This is also visible in Figure 3A. Is it possible that disruption of SDS-22 reduces cortical flows (time, intensity or duration) and could this explain the small reduction in anterior PAR-2 spreading and thus the slightly smaller domain size measured in Figures 1B and 3A.
We have noticed that SDS-22 depletion results in less ruffling and reduced pseudocleavage furrows. To properly address this question we should have a condition in which we can rescue the cortical flow reduction in the SDS-22 depletion and measure the PAR-2 domain. Since we do not know how SDS-22 reduces the flows, we could not come up with a clean experiment to address this issue and are happy to have suggestions.
We believe that the most rigorous way to address this issue, as reviewer 1 points out, is to clearly address this limitation in the text. We have now added this in the discussion:
Discussion Line 463-466, page 18:
Consistent with GSP-2 reduced levels, SDS-22 depleted or E153A mutant embryos also have a smaller PAR-2 domain. However, since these embryos also show reduced cortical ruffling (Movie EV1,2) and are smaller (Fig EV2C) we cannot exclude that these two phenotypes also contribute to the smaller size of the PAR-2 domain.
- *
A potentially related issue could be embryo size. sds-22 embryos generally seem to be smaller than wild-type (e.g. Figure 1B(left), 4A(left column), and particularly EV3). Is this consistently true? Could cell size effects change the ability of embryos to clear anterior PAR-2 domains as described in EV3? Klinkert et al (2018, biorXiv) note that reducing the size of air-1(RNAi) embryos reduces the frequency of bipolar PAR-2 domains.
Quantification of perimeter of embryos at pronuclear meeting in live zygotes. Sample size (n) is indicated in the graph, each dot represents a single embryo and mean is shown. N = 5. The P value was determined using two-tailed unpaired Student’s t test.
We quantified the perimeter of the embryos and as seen by quantification, there is a weak but significant decrease of size in the absence of SDS-22, and in SDS-22(E153A) mutant, as shown above. We have now added the data of the RNAi in the supplementary information and mentioned it in the results.
Results Line 129, page 5:
SDS-22 depleted embryos also displayed a smaller size (Fig EV2C).
Klinkert et al reported that reducing the size of air-1(RNAi) embryos by depletion of ANI-2, a homolog of the actomyosin scaffold protein anillin, reduces the frequency of bipolar PAR-2 domains (Klinkert et al, 2018). In the image shown in the paper on bioRxiv, the PAR-2 domain appears small but there are no quantifications and these data have been removed from the published paper.
From published data, a smaller embryo size does not appear to correlate with smaller PAR-2 domain. Chartier et al show that depletion of ANI-2 reduces embryo size without changing the relative anterior PAR-6 domain (Chartier et al, 2011), thereby suggesting that the posterior PAR-2 domain should not change either. In addition, Hubatsch et al reported that small embryos depleted of ima-3 tend to have larger PAR-2 domains, whereas larger embryos depleted of C27D9.1 exhibit smaller PAR-2 domains (Hubatsch et al, 2019), which is the opposite of what we see. We do not believe that the smaller PAR-2 domain is the important message of our paper. Our main question was whether PAR-2 was cortical or not and since GSP-2 had a smaller domain, we decided to quantify the PAR-2 domain length in the different RNAi conditions and mutants. Since RNAi of C27D9.1 which makes embryos bigger, results in a small PAR-2 domain, again we do not know how to experimentally address this question, unless the reviewer has a suggestion. As for the point above, we will clearly highlight this limitation in the discussion (see our reply to the previous point, now it is in Discussion Line 463-466, page 18).
We would stress that these comments relate to interpreting the polarity phenotypes and do not undermine the core finding that SDS-22 stabilises GSP-1/2.
We thank the reviewer and we hope that by performing the experiments mentioned above and by changing the text, their comments are properly addressed.
Reviewer 2
Major comment: Consistent with the model that PP1 activity is reduced in the absence of SDS-22, the authors show that a surrogate PP1 target (phospho-histone H3) becomes hyper-phosphorylated. To strengthen the study, the authors could consider performing an OPTIONAL experiment (see below) of assaying the phosphorylation status of PAR-2 itself, as this is proposed to be the target of both PKC-3 and PP1, and represent the mechanism of PAR-2 polarization.
We thank the reviewer for this comment and also for pointing out that there is technical difficulty in the proposed experiment.
We have already attempted to address this point without success in Calvi et al (Calvi et al, 2022), using western blot analysis (see below). For this we used the GFP::PAR-2 strain and used a GFP antibody (shown below in the left panel), as none of the anti-PAR-2 antibodies (neither the ones produced by us nor the ones produced by other laboratories) were working on western blot. We observed several bands of GFP::PAR-2 but were not able to determine if these represented phosphorylated forms or to compare the ratio of phosphorylated to unphosphorylated PAR-2. We did use λ-PPase in the embryonic extracts but we did not always observe a clear difference. We show three experiments below.
Left, __Western blots of gfp::par-2 embryonic extract in the presence or absence of λ-PPase (+/- PhosSTOP) and probed with anti-GFP and anti-Tubulin antibodies. Right,__ Representative images of fixed embryos with indicated genotypes at one-, two- and four-cell stages. DNA (DAPI) is gay. Scale bars, 5 μm. Anterior is to the left and posterior to the right.
One possible explanation is that the role of GSP-1/-2 in PAR-2 dephosphorylation is specific to the very early embryos. As shown in the right panel above, despite PAR-2(RAFA) remaining cytoplasmic in one- and two-cell embryos due to lack of binding to GSP-1/-2, it can localize to internal cortices in four-cell stage embryos, similarly to the control and suggesting that in later embryos other mechanisms are intervening. One limitation of our Western Blot is that it is not possible to isolate only early embryos, which are a minority in a mixed population of embryos. This may mask difference of phosphorylation status of PAR-2 in the early stages.
For the revision, we plan to blot PAR-2 using GFP antibody in gfp::par-2 embryo lysates, with both control and sds-22(RNAi) treatment. We will also compare the GFP::PAR-2 bands between gfp::par-2 and gfp::par-2; sds-22(E153A) mutant samples. We are not very hopeful and our failures with gsp-1/2 RNAi (unpublished) are why we did not try with SDS-22 but it is definitely worth giving it a go and we will.
As for Hao et al (Hao et al, 2006) the result was quite clear. In this paper however, the authors used a transgene strain of PAR-2. We have never tried to use a transgene (the proteins are usually overexpressed) but we can deplete SDS-22 in a PAR-2 transgene as well and see if a difference is observed.
Reviewer 3
Major comments: major issues affecting the conclusions
Overall, the authors' conclusions are supported by their data. The data and methods are presented clearly, with appropriate replicates and statistics. Here I propose two experiments to strengthen the link between some of their data and their claims. These experiments could take a month or two to complete.
Experiment 1
It would be helpful if the authors could show that blocking the proteasome in the zygote restores GSP-1/-2 levels in the absence of SDS-22 or even better in the SDS-22(E153A) mutant. This would provide more direct evidence to support their claim that SDS-22 regulates polarity by protecting PP1 from proteasomal degradation. While they are currently conducting this experiment in the germline, they cannot assess polarity there. However, in the zygote, they would be able to examine the PAR-2 domain (polarity). To do this, the authors could permeabilise the embryos and apply a proteasome inhibitor.
This would be a straightforward experiment if we were using culture cells. One problem with the set up is that much of the protein of the one-cell embryo is inherited from the egg and the reduction in SDS-22 depletion or mutant happens already in the germline (Fig 6-7). Even if the proteasome is inhibited in embryos, the whole division process only takes 20 minutes and we wonder whether the timing will be sufficient to inhibit the proteasome, produce more protein and rescue the phenotype. We will try, as only this will tell us.
One alternative approach would be to apply the proteasome inhibitor to adult worms in liquid culture for several hours before dissection. This would aim to inhibit degradation in the germline, therefore allowing us to test whether GSP-1/-2 levels are restored in the embryos with SDS-22 disruption. However, proteasome inhibition in the germline impairs oogenesis (Shimada et al, 2006), suggesting that we might incur in the same problem (unless we succeed in timing the inhibition).
One additional experiment that we will try is to deplete other proteasomal subunits that result in a lower level or proteasomal activity reduction. As reported by Fernando et al (Fernando et al, 2022), depletion of RPN-9, -10, or -12 impairs proteasomal activity, but worms remain fertile.
Quantification of mNG::GSP-2 and GFP::GSP-1fluorescence intensity in rpn-12, rpn-9, and rpn-10(RNAi) normalized to ctrl(RNAi). Mean is shown and error bars indicate SD. Dots in graphs represent individual embryo measurements and sample size (n) is indicated inside the bars in the graph. N = 1.
So far, our data suggest that the GSP-1/-2 levels are weakly but significantly increased in the embryos (16.8% for GSP-2 and 12.5% for GSP-1) following RPN-12 depletion (see above). We will co-deplete RPN-12 and SDS-22 to assess if the protein levels of GSP-1/-2 are rescued. We will also deplete RPN-12 in gfp::gsp-1; sds-22(E153A) strains to test if GSP-1 levels are rescued. We cannot measure GSP-2 levels in mNG::GSP-2; sds-22(E153A) because they are embryonic lethal (see details below in the reply to minor comments of Reviewer 3).
Left, Representative midsection images of gfp::gsp-1 and gfp::gsp-1;sds-22(E153A) embryos in ctrl(RNAi) and rpn-12(RNAi).__ Right, __Quantification of GFP::GSP-1 intensity levels. N = 1.
Our preliminary data showed that similar to germlines (Fig 7G-I), RPN-12 depletion in gfp::gsp-1; sds-22(E153A) rescued the reduction of GSP-1 levels in embryos (shown above). We will perform two additional experiments to quantify GSP-1 levels.
We will also test if the smaller PAR-2 domain in sds-22(E153A) mutant is rescued by RPN-12 depletion. With these experiments, we aim to answer if proteasome inhibition rescues the reduced levels of GSP-1/-2 and thereby rescues the reduced PAR-2 domain when SDS-22 is depleted or mutated.
Experiment 2
The posterior localization of PAR-2 after co-RNAi of GSP-1 and SDS-22 contrasts with the absence of PAR-2 at the cortex when both GSP-1 and GSP-2 are depleted. This difference may be due to the partial reduction of GSP-2 levels when SDS-22 is depleted, compared to the more substantial reduction of GSP-2 upon GSP-2 RNAi. Have the authors considered combining full depletion of GSP-1 with partial depletion of GSP-2 to see if PAR-2 remains present and localized to the posterior? This experiment could help clarify the discrepancy between the phenotypes and further support the role of SDS-22 in regulating GSP-2 protein levels. Additionally, by titrating PP1, the authors may be able to determine the minimum amount of PP1 needed to establish the PAR-2 domain.
We will try this experiment but, assuming we find a condition in which we can fully deplete GSP-1 and only half of GSP-2, one problem is that it is impossible to control the levels of both GSP-1 and 2 and measure the PAR-2 domain in the same embryos (which would be the most rigorous way to perform the experiment so that we know the amount of depletion and correlate with the PAR-2 domain length). The only thing we can do is the same depletion time in the 3 different strains (the mNG::gsp-2, the gfp::gsp-1 and the gfp::par-2) and assume that the depletion will work the same in the three different strains.
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Minor comments
Reviewer 1
Minor Points
- The link between lethality and polarity of the zygote is not always obvious and whether they are connected (or not) could probably be made clearer. Indeed, the source of lethality is unclear, particularly given that loss of SDS-22 on its own strongly impacts lethality with minimal effects on polarity (at least in the zygote).
In many cases, we have reported embryonic lethality as information, not with a precise scope to correlate the lethality with the phenotype. We apologize for the lack of clarity. We know that embryonic lethality is normally associated with severe polarity defects. As example, in the par-2(RAFA) mutant and in the pkc-3ts mutant at temperatures around 24-25°C cortical polarity is lost, embryos divide symmetrically and synchronously and die (Calvi et al., 2022; Rodriguez et al, 2017) and many more references for the PAR mutants (Kemphues et al, 1988; Kirby et al, 1990; Morton et al, 1992). We and others have also shown that depletion of GSP-2 can rescue the lethality of pkc-3(ts) but only at a semipermissive temperature when there is still residual PKC-3 activity (Calvi et al., 2022; Fievet et al, 2013). As our aim was to identify the regulator of GSP-2, we tested the potential regulators by RNAi in the pkc-3(ts), with the assumptions that a regulator, similar to GSP-2, would rescue the pkc-3(ts) polarity defects and lethality. As it turns out, SDS-22 is not a canonical regulator of GSP-2. The partial rescue of the polarity defects is most likely the result of the fact that SDS-22 lowers the level of GSP-2. However, SDS-22 is probably involved in many other functions that involve GSP-1 and GSP-2 (as shown for example:(Beacham et al, 2022; Peel et al., 2017)) and it is embryonic lethal. We do not know, however, whether the embryonic lethality is the results of the sum of the various functions of SDS-22 or it is due to a specific function.
To clarify it better, we have now explained the connection between polarity and lethality in the text,
From Result Line 111-114, page 5:
We first asked whether depletion of any of these three regulators suppress the embryonic lethality of pkc-3(ne4246); gfp::par-2 embryos at the semi-permissive temperature of 24°C (in which PKC-3 is partially active, temperature used in all experiments with the pkc-3(ne4246) mutant, unless otherwise stated), similar to depletion of the catalytic subunit GSP-2.
To Results Line 111-117, page 5:
*When the temperature sensitive mutant pkc-3(ne4246) is grown at semi-permissive temperature, the residual PKC-3 activity is not sufficient to exclude PAR-2 from the anterior cortex. These embryos cannot establish polarity and die. Depletion of the catalytic subunit GSP-2 in this strain suppresses PAR-2 mislocalization and the resulting polarity defects, thereby rescuing embryonic lethality. We first asked whether depletion of any of these three identified regulators suppresses the embryonic lethality of pkc-3(ne4246); gfp::par-2 embryos at the semi-permissive temperature of 24°C (temperature used in all experiments with the pkc-3(ne4246) mutant, unless otherwise stated) , similar to depletion of GSP-2. *
From Result Line 241-242, page 10:
We next asked whether sds-22(E153A) was able to rescue the lethality and the polarity defects of pkc-3(ne4246) embryos.
To Results Line 223-224, page 9:
Because of this, we decided to test whether sds-22(E153A) was able to rescue the lethality and the polarity defects of pkc-3(ne4246) embryos.
- Formally, the conclusion that reduced GSP-1/2 in SDS-22 depletion conditions is due to increased proteasomal degradation is not shown directly as there is no data on rates just steady-state levels. We agree that the genetic data is strongly suggestive of this model and it is consistent with work of other labs. Thus this is the most likely scenario, but could in principle reflect reduced expression that is balanced by reduced degradation.
We agree with the reviewer. To address this point, we will perform RT-PCR analysis to measure the gene expression levels of gsp-1 and gsp-2 from control, SDS-22 depletion and sds-22(E153A) embryos.
- It is interesting that sds-22(E153A) caused a stronger decrease in oocyte GSP-1 levels than sds-22(RNAi) (Fig 7). The authors may want to comment on this result.
As we performed depletion of SDS-22 by RNAi feeding from L4 stage, we might not see strong reduction of GSP-1 in oocytes compared to that in sds-22(E153A) mutant, which carries an endogenous mutation of SDS-22 throughout the life cycle.
Left, Representative images of gfp::gsp-1 germlines in ctrl(RNAi) and sds-22(RNAi), comparing to gfp::gsp-1; sds-22(E153A); ctrl(RNAi). __Right, __Quantification of GFP::GSP-1 intensity levels in the cytoplasm and nucleus of -1 and -2 oocytes. N = 1.
To address this point we have performed an experiment where we have depleted SDS-22 starting from L1s. As shown above, RNAi feeding of SDS-22 from L1 stage showed a similar reduction of GSP-1 (16.1% in the cytoplasm; 24.6% in the nucleus) as in gfp::gsp-1; sds-22(E153A), which was stronger comparing to feeding from L4 (8.8% in the cytoplasm; 17.4% in the nucleus, Fig 7D-E). This supports our hypothesis that the difference shown in Fig 7D-I might result from a relative short RNAi depletion of SDS-22 from L4 stage comparing to endogenous SDS-22(E153A) mutation. This experiment was done only once and will be repeated. If confirmed, we will add a sentence in the text. As RNAi feeding of SDS-22 from L1 stage impairs the formation of germlines, we will keep the protocol using SDS-22 RNAi feeding in L4 worms for other experiments in this study.
- "At polarity establishment, the PP1 phosphatases GSP-1/-2 dephosphorylate PAR-2 allowing its cortical posterior accumulation." This statement, possibly inadvertently, implies temporal regulation, which has not been shown.
We have changed the sentence, as suggested by the reviewer:
To Introduction Line 59-60, page 3:
The PP1 phosphatases GSP-1/-2 dephosphorylate PAR 2 allowing its cortical posterior accumulation and embryo polarization.
- It would be ideal if the authors could explicitly state how they define pronuclear meeting. For example in Figure 1B, the embryos look like they are a few minutes past pronuclear meeting (e.g. compared to Figure 3), but maybe the pronuclei tend to meet more centrally in these conditions? Given that PAR-2 clearance is changing in time in some of these cases (based on looking at the movies), staging needs to be very accurate to get the best comparisons.
We apologize for the lack of clarity. Pronuclear meeting is defined when the two pronuclei first contact each other.
As noted by Reviewer 1, it is true that the pronuclei in pkc-3ts mutant tend to meet more centrally compared to control embryos. The same finding was also observed on PKC-3 inhibition (through depletion, mutation or inhibitor treatment) by Rodriguez et al (Rodriguez et al., 2017). In addition, Kirby et al reported that mutations in the anterior PAR complex lead to the mislocalization of the pronuclei, causing them to meet more in the center (Kirby et al., 1990). We now specify this in the Material and Methods.
Add in Material and Methods Line 633-635, page 22:
*The stage of pronuclear meeting is defined when the two pronuclei first contact each other. In pkc-3(ne4246) embryos, the two pronuclei exhibited a tendency to meet more centrally compared to controls (Fig 1B, Movie EV1), as shown in (Kirby et al, 1990; Rodriguez et al, 2017). *
As Reviewer 1 mentioned, accurate staging is crucial, as PAR-2 clearance can vary over time. The measurements were done in the first frame where pronuclei touch each other. However, in Fig. 1B we had shown one pkc-3ts; sds-22(RNAi) embryo one frame (10 seconds) later. We have now corrected this (see the updated Figure 1B).
- In the interests of data-availability, upon publication the authors would deposit the raw mass spec data underlying Figure EV1.
The reviewer is right, this was forgotten. We have now added as supplementary material the Dataset EV1 and EV2.
Reviewer 3
Minor comments: important issues that can confidently be addressed
In the introduction (line 83), it's unclear what reconciles the contradictory data. I also have difficulty understanding this point in the discussion (line 435).
We apologize for the lack of clarity and have now modified the text:
From Introduction Line 82-84, page 4:
This underscores the complex roles of SDS22 in regulating PP1 function and reconciling the contradictory data obtained in vivo and in vitro (Cao et al., 2024; Cao et al, 2022; Kueck et al., 2024; Lesage et al, 2007).
To Introduction Line 81-85, page 4:
These two recent findings suggest that while SDS-22 is required for the biogenesis of PP1 holoenzymes, its removal is essential to have an active PP1. This dual role of SDS-22 explains how SDS22 behaves as an inhibitor in biochemical assays in vitro but as an activator in vivo (Cao et al., 2024; Cao et al, 2022; Kueck et al., 2024; Lesage et al, 2007).
From Discussion Line 435-436, page 17:
These data reconcile the contradictory in vivo and in vitro observations.
To Discussion Line 447-451, page 17:
Given that SDS-22 both stabilizes PP1 levels and inhibits its activity, this dual role clarifies the apparent contradiction: while SDS-22 is essential for PP1 activity in vivo (because it is essential for the biogenesis/stability), it inhibits PP1 activity in vitro (as it needs to be removed to have an active PP1), while in vivo it is removed by p97/Valosin resulting in active PP1.
Additionally, in the results section (line 389), it's not clear why the gonads cannot be studied in the strain with dead embryos. Are the gonads also altered in a way that prevents their observation?
We explained this in the material and methods part (Line 583-584, 588-592), page 21.
To clarify it better in the main text, we have now modified
Results Line 377-378, page 15:
Since depletion of these subunits results in worms with very little to no progeny (Fernando et al., 2022)
Results Line 396-401, page 15:
*Since we use the embryonic lethality phenotype of the mNG::gsp-2; sds-22(E153A) strain to recognize the homozygote sds-22(E153A), this precluded the possibility to analyze the germlines of homozygote mNG::gsp-2; sds-22(E153A) worms depleted of RNP-6.1 or RPN-7, as these worms do not have progenies (Fernando et al., 2022) and we therefore cannot distinguish the sds-22(E153A) homozygote from the sds-22(E153A) heterozygote (see material and methods for details). *
3. Description of the revisions that have already been incorporated in the transferred manuscript
Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. If no revisions have been carried out yet, please leave this section empty.
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We have re-quantified the data in Fig 1B and displayed as in Fig 1C.
We have double checked our data and corrected Fig 3G.
We have modified the text to address many of the comments of the reviewer about clarity and rigor.
We have added supplementary information Fig EV2C and Dataset EV1 and EV2.
Other experiments performed are still preliminary and only shown in this revision letter.
4. Description of analyses that authors prefer not to carry out
Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.
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We believe with the reply, the text changes and the experiments that we have proposed and started, we will address all comments of the reiewers.
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References
Beacham GM, Wei DT, Beyrent E, Zhang Y, Zheng J, Camacho MMK, Florens L, Hollopeter G (2022) The Caenorhabditis elegans ASPP homolog APE-1 is a junctional protein phosphatase 1 modulator. Genetics 222
Calvi I, Schwager F, Gotta M (2022) PP1 phosphatases control PAR-2 localization and polarity establishment in C. elegans embryos. J Cell Biol 221
Chartier NT, Salazar Ospina DP, Benkemoun L, Mayer M, Grill SW, Maddox AS, Labbe JC (2011) PAR-4/LKB1 mobilizes nonmuscle myosin through anillin to regulate C. elegans embryonic polarization and cytokinesis. Curr Biol 21: 259-269
Fernando LM, Quesada-Candela C, Murray M, Ugoaru C, Yanowitz JL, Allen AK (2022) Proteasomal subunit depletions differentially affect germline integrity in C. elegans. Front Cell Dev Biol 10: 901320
Fievet BT, Rodriguez J, Naganathan S, Lee C, Zeiser E, Ishidate T, Shirayama M, Grill S, Ahringer J (2013) Systematic genetic interaction screens uncover cell polarity regulators and functional redundancy. Nat Cell Biol 15: 103-112
Hao Y, Boyd L, Seydoux G (2006) Stabilization of cell polarity by the C. elegans RING protein PAR-2. Dev Cell 10: 199-208
Hubatsch L, Peglion F, Reich JD, Rodrigues NT, Hirani N, Illukkumbura R, Goehring NW (2019) A cell size threshold limits cell polarity and asymmetric division potential. Nat Phys 15: 1075-1085
Kemphues KJ, Priess JR, Morton DG, Cheng NS (1988) Identification of genes required for cytoplasmic localization in early C. elegans embryos. Cell 52: 311-320
Kirby C, Kusch M, Kemphues K (1990) Mutations in the par genes of Caenorhabditis elegans affect cytoplasmic reorganization during the first cell cycle. Dev Biol 142: 203-215
Klinkert K, Levernier N, Gross P, Gentili C, von Tobel L, Pierron M, Busso C, Herrman S, Grill SW, Kruse K et al (2018) Aurora A depletion reveals centrosome-independent polarization mechanism in C.elegans. bioRxiv: 388918
Morton DG, Roos JM, Kemphues KJ (1992) par-4, a gene required for cytoplasmic localization and determination of specific cell types in Caenorhabditis elegans embryogenesis. Genetics 130: 771-790
Park SH, Cheong C, Idoyaga J, Kim JY, Choi JH, Do Y, Lee H, Jo JH, Oh YS, Im W et al (2008) Generation and application of new rat monoclonal antibodies against synthetic FLAG and OLLAS tags for improved immunodetection. J Immunol Methods 331: 27-38
Peel N, Iyer J, Naik A, Dougherty MP, Decker M, O'Connell KF (2017) Protein Phosphatase 1 Down Regulates ZYG-1 Levels to Limit Centriole Duplication. PLoS Genet 13: e1006543
Rodriguez J, Peglion F, Martin J, Hubatsch L, Reich J, Hirani N, Gubieda AG, Roffey J, Fernandes AR, St Johnston D et al (2017) aPKC Cycles between Functionally Distinct PAR Protein Assemblies to Drive Cell Polarity. Dev Cell 42: 400-415 e409
Shimada M, Kanematsu K, Tanaka K, Yokosawa H, Kawahara H (2006) Proteasomal ubiquitin receptor RPN-10 controls sex determination in Caenorhabditis elegans. Mol Biol Cell 17: 5356-5371
Tzur YB, Egydio de Carvalho C, Nadarajan S, Van Bostelen I, Gu Y, Chu DS, Cheeseman IM, Colaiacovo MP (2012) LAB-1 targets PP1 and restricts Aurora B kinase upon entrance into meiosis to promote sister chromatid cohesion. PLoS Biol 10: e1001378
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overreacted.io overreacted.io
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Overview & Motivation
Repeatedly failed to write a post, realizing it should be a talk:
“It turns out that I wasn’t really writing a post; I was actually preparing a talk.”
Central Topic: React Server Components and distributed computations between two machines using React concepts.
“It’s about everyone’s favorite topic, React Server Components.”
Act 1: Recipes (Imperative) vs. Blueprints (Declarative)
Tags vs. Function Calls:
Visual and structural differences:
“< and > are hard and spiky and ( and ) are soft and round.”
Similarities:
Both reference named operations (functions or tags) and accept arguments.
Both allow nesting.
“Clearly, function calls and tags are very similar...they let us elaborate by nesting further.”
Differences:
Tags (declarative):
Often nouns; represent timeless structures (blueprints).
Convenient for deep nesting, clearly marking structure.
Time-independent, passive descriptions.
“Tags tend to be nouns rather than verbs... nouns are easier to decompose.”
Function calls (imperative):
Often verbs; represent sequential actions (recipes).
Execution order critical.
“A recipe prescribes a sequence of steps to be performed in order.”
Remote Procedure Calls (RPC) and Async/Await
Problem: Calling Functions Across Computers
RPC concept introduced: Functions across network boundaries.
async/await: Simplifies asynchronous calls but still has limitations (coupling, losing direct references).
“An async function...may pause execution...async and await propagate upwards.”
Import RPC idea: Extends importing to remote function calls while maintaining references and type-checking.
“Let’s invent a special syntax...import rpc because what we’ve described here has been known for decades as RPC.”
Potential Calls (Tags as Deferred RPCs)
"Potential function calls": Represented by tags; calls that might happen in the future.
“It’s a blueprint of a function call.”
Nested tags: Express dependencies naturally.
“Dependencies between potential calls...should be expressed by embedding these calls inside each other.”
Splitting Computation in Time and Space
Computation split in time: Returning partial functions that capture necessary data (closures).
Computation split across space (client-server): Splitting execution between two computers, handling data passing explicitly.
“It’s an interesting shape—a program returning the rest of itself...closure over the network.”
Two Types of Operations: Components vs. Primitives
Components (Capitalized): "Brains" of a program; flexible, timeless, and declarative, embedding tags without introspection.
“Components are truly timeless...they accept tags as arguments.”
Primitives (lowercase): "Muscles"; introspect arguments, execution order sensitive, imperative, execute last.
“Primitives introspect arguments...they must know all their arguments.”
Execution Phases:
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Interpret (thinking): Processes Components freely without strict order.
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Perform (doing): Executes Primitives strictly inside-out.
“First, you need to think...then you need to do.”
Act 2: Reflections and Dialog
Meta-dialog: Reflection on the writing process itself; writer and reader dialogue, acknowledging uncertainty and experimental nature of content.
“The Writer: I have a rough idea, but truthfully, I’m pretty much winging it.”
Core Conceptual Innovations
Tags as code/data pairs: Potential function calls represented explicitly as data (tags), allowing deferred execution across contexts.
Program as distributed computation: A single conceptual function spanning multiple runtime environments (Early and Late worlds).
Timelessness and Flexibility: Components allow arbitrary computation ordering; Primitives enforce execution order.
Key Quotes & Ideas:
Blueprints vs. Recipes:
“A blueprint describes what nouns a thing is made of...a recipe prescribes a sequence of steps to be performed.”
RPC and Potential Calls:
“A tag is like a function call but passive, inert, open to interpretation.”
Components and Primitives Separation:
“Components are the ‘brains’...Primitives are the ‘muscles’.”
Importance of Introspection vs. Embedding:
“If a function only embeds an argument without introspection, you can delay computing it.”
Conclusion (Conceptual Breakthroughs)
Distributed React Model: Redefining client-server interaction as React component structures.
Future implications: Suggests moving common primitives into lower-level implementations to optimize distributed computation.
“If many programs used the same Primitives...move their implementation to Rust or C++.”
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www.biorxiv.org www.biorxiv.org
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Author response:
The following is the authors’ response to the original reviews
Public Reviews:
Reviewer #1 (Public review):
This a comprehensive study that sheds light on how Wag31 functions and localises in mycobacterial cells. A clear link to interactions with CL is shown using a combination of microscopy in combination with fusion fluorescent constructs, and lipid specific dyes. Furthermore, studies using mutant versions of Wag31 shed light on the functionalities of each domain in the protein. My concerns/suggestions for the manuscript are minor:
(1) Ln 130. A better clarification/discussion is required here. It is clear that both depletion and overexpression have an effect on levels of various lipids, but subsequent descriptions show that they affect different classes of lipids.
We thank the reviewer for the comment. We have added a better clarification on this in the discussion of revised manuscript. The lipid classes that get impacted by the depletion of Wag31 vs overexpression are different. Wag31 is an adaptor protein that interacts with proteins of the ACCase complex (Meniche et al., 2014; Xu et al., 2014) that synthesize fatty acid precursors and regulate their activity (Habibi Arejan et al., 2022).
The varied response on lipid homeostasis could be attributed to a change in the stoichiometry of these interactions of Wag31. While Wag31 depletion would prevent such interactions from occurring and might affect lipid synthesis that directly depends on Wag31-protein partner interactions, its overexpression would lead to promiscuous interactions and a change in the stoichiometry of native interactions that would ultimately modulate lipid synthesis pathways.
(2) The pulldown assays results are interesting, but links are tentative.
We thank the reviewer for the comment. The interactome of Wag31 was identified through the immunoprecipitation of FLAG-Wag31 complemented at an integrative locus in Wag31 mutant background to avoid overexpression artifacts. We used Msm::gfp expressing an integrative copy (at L5 locus) of FLAG-GFP as a control to subtract non-specific interactions. The experiment was performed in biological triplicates, and interactors that appeared in all replicates but not in the control were selected for further analysis. Although we identified more than 100 interactors of Wag31, we analyzed only the top 25 hits, with a PSM cut-off 18 and unique peptides5. Additionally, two of Wag31's established interactors, AccD5 and Rne, were among the top five hits, thus validating our data.
As mentioned in line 139 of the previous version of the manuscript, we agree that the interactions can either be direct or through a third partner. The fact that we obtained known interactors of Wag31 makes us believe these interactions are genuine. Moreover, for validation, we performed pulldown experiments by mixing E. coli lysates expressing His-Wag31 full-length or truncated protein with M. smegmatis lysates expressing FLAG-tagged interacting proteins. The wash conditions used were quite stringent for these pull-down assays—the wash buffer contained 1% Triton X100 that eliminates all non-specific and indirect interactions. However, we agree that we cannot conclusively state that the interactions are direct without purifying the proteins and performing the experiment. As mentioned above, this caveat was stated in the previous version of the manuscript.
(3) The authors may perhaps like to rephrase claims of effects lipid homeostasis, as my understanding is that lipid localisation rather than catabolism/breakdown is affected.
We thank the reviewer for the comment. In this manuscript, we are trying to convey that Wag31 is a spatiotemporal regulator of lipid metabolism. It is a peripheral protein that is hooked to the membrane via Cardiolipin and forms a scaffold at the poles, which helps localize several enzymes involved in lipid metabolism.
Homeostasis is the process by which an organism maintains a steady-state of balance and stability in response to changes. Depletion of Wag31 not only results in delocalisation of lipids in intracellular lipid inclusions but also leads to changes in the levels of various lipid classes. Advancement in the field of spatial biology underscores the importance of native localization of various biological molecules crucial for maintaining a steady-cell of the cell. Hence, we have used the word “homeostasis” to describe both the changes observed in lipid metabolism.
Reviewer #2 (Public review):
Summary:
Kapoor et. al. investigated the role of the mycobacterial protein Wag31 in lipid and peptidoglycan synthesis and sought to delineate the role of the N- and C- terminal domains of Wag31. They demonstrated that modulating Wag31 levels influences lipid homeostasis in M. smegmatis and cardiolipin (CL) localisation in cells. Wag31 was found to preferentially bind CL-containing liposomes, and deleting the N-terminus of the protein significantly decreased this interaction. Novel interactions between Wag31 and proteins involved in lipid metabolism and cell wall synthesis were identified, suggesting that Wag31 recruits proteins to the intracellular membrane domain by direct interaction.
Strengths:
(1) The importance of Wag31 in maintaining lipid homeostasis is supported by several lines of evidence. (2) The interaction between Wag31 and cardiolipin, and the role of the N-terminus in this interaction was convincingly demonstrated.
Weaknesses:
(1) MS experiments provide some evidence for novel protein-protein interactions. However, the pulldown experiments lack a valid negative control.
We thank the reviewer for the comment. We have included two non-interactors of Wag31 i.e. MmpL4 and MmpS5 which were not identified in our interactome database as negative controls in the experiment. As shown in Figure S3, we performed His pull-down experiments with both of them independently twice, each time with a positive control (known interactor of Wag31 (Msm2092)). Fig. S3b revised shows E. coli lysate expressing His-Wag31 which was incubated with Msm lysates expressing either FLAG tagged-MmpL4 or -MmpS5 or Msm2092 (revised Fig. S3c). The mixed lysates were pulled down with Cobalt beads that bind to the His-tagged protein and analysed using Western blot analysis by probing with anti-FLAG antibody (revised Fig. S3d.). The data presented confirms that the interactions validated through the pull down assay were indeed specific.
(2) The role of the N-terminus in the protein-protein interaction has not been ruled out.
We thank the reviewer for the comment. Wag31<sub>Msm</sub> is a 272 amino acids long protein. The Nterminal of Wag31, which houses the DivIVA-domain, comprises the first 60 amino acids. Previously, we attempted to express the N-terminal (60 aa long) and the C-terminal (212 aa long) truncated proteins in various mycobacterial shuttle vectors to perform MS/MS experiments. Despite numerous efforts, neither expressed with the N/C-terminal FLAG tag or no tag in episomal or integrative vectors due to instability of the protein. Eventually, we successfully expressed the C-terminal Wag31 with an N and Cterminal hexa-His tag. However, this expression was not sufficient or stable enough for us to perform Ni<sup>2+</sup>-affinity pull-down experiments for mass spectrometry. N-terminal of Wag31 could not be expressed in M. smegmatis even with N and C-terminal Hexa-His tags.
To rule out the role of the N-terminal in mediating protein-protein interactions, we cloned the N-terminal of Wag31 that comprises the DivIVA-domain in pET28b vector (Fig. 7a revised). Subsequently, the truncated protein, hereafter called Wag31<sub>∆C</sub> flanked by 6X His tags at both the termini was expressed in E. coli and mixed with Msm lysates expressing interactors of Wag31 (Fig. 7b-c revised). Earlier experiments with Wag31<sub>∆1-60</sub or Wag31<sub>∆N</sub> (in the revised manuscript) were performed with MurG, SepIVA, Msm2092 and AccA3 (Fig. 7e-g). Thus, we used the same set of interactors to test our hypothesis. Briefly, His- Wag31<sub>∆C</sub> was mixed with Msm lysates expressing either FLAG-MurG, -SepIVA, -Msm2092 or -AccA3 and pull down experiments were performed as described previously. FLAGMmpS5, a non-interactor of Wag31 was used as a negative control. As shown in Fig. 7d revised, His-Wag31 could bind to all the four interactors whereas His- Wag31<sub>∆C</sub> couldn’t, strengthening the conclusion that interactions of Wag31 with other proteins are mediated by its Cterminal. However, we can’t ignore the possibility of other interactors binding to the N-terminal of Wag31. Unfortunately, due to poor expression/instability of Wag31<sub>∆C</sub> in mycobacterial shuttle vectors, we are unable to perform a global interactome analysis of Wag31<sub>∆C</sub>
Reviewer #3 (Public review):
Summary:
This manuscript describes the characterization of mycobacterial cytoskeleton protein Wag31, examining its role in orchestrating protein-lipid and protein-protein interactions essential for mycobacterial survival. The most significant finding is that Wag31, which directs polar elongation and maintains the intracellular membrane domain, was revealed to have membrane tethering capabilities.
Strengths:
The authors provided a detailed analysis of Wag31 domain architecture, revealing distinct functional roles: the N-terminal domain facilitates lipid binding and membrane tethering, while the C-terminal domain mediates protein-protein interactions. Overall, this study offers a robust and new understanding of Wag31 function.
Weaknesses:
The following major concerns should be addressed.
• Authors use 10-N-Nonyl-acridine orange (NAO) as a marker for cardiolipin localization. However, given that NAO is known to bind to various anionic phospholipids, how do the authors know that what they are seeing is specifically visualizing cardiolipin and not a different anionic phospholipid? For example, phosphatidylinositol is another abundant anionic phospholipid in mycobacterial plasma membrane.
We thank the reviewer for the comment. Despite its promiscuous binding to other anionic phospholipids, 10-N-Nonyl-acridine orange is widely used to stain Cardiolipin and determine its localisation in bacterial cells and mitochondria of eukaryotes (Garcia Fernandez et al., 2004; Mileykovskaya & Dowhan, 2000; Renner & Weibel, 2011). This is because it has a stronger affinity for Cardiolipin than other anionic phospholipids with the affinity constant being 2 × 10<sup>6</sup> M−<sup>1</sup> for Cardiolipin association and 7 × 10<sup>4</sup> M−<sup>1</sup> for that of phosphatidylserine and phosphatidylinositol association (Petit et al., 1992). Additionally, there is not yet another stain available for detecting Cardiolipin. Our proteinlipid binding assays suggest that Wag31 preferentially binds to Cardiolipin over other anionic phospholipids (Fig. 4b), hence it is likely that the majority of redistribution of NAO fluorescence that we observe might be contributed by Cardiolipin mislocalization due to altered Wag31 levels, with smaller degree of NAO redistribution intensity coming indirectly from other anionic phospholipids displaced from the membrane due to the loss of membrane integrity and cell shape changes due to Wag31.
• Authors' data show that the N-terminal region of Wag31 is important for membrane tethering. The authors' data also show that the N-terminal region is important for sustaining mycobacterial morphology. However, the authors' statement in Line 256 "These results highlight the importance of tethering for sustaining mycobacterial morphology and survival" requires additional proof. It remains possible that the N-terminal region has another unknown activity, and this yet-unknown activity rather than the membrane tethering activity drives the morphological maintenance. Similarly, the N-terminal region is important for lipid homeostasis, but the statement in Line 270, "the maintenance of lipid homeostasis by Wag31 is a consequence of its tethering activity" requires additional proof. The authors should tone down these overstatements or provide additional data to support their claims.
We agree with the reviewer that there exists a possibility for another function of the N-terminal that may contribute to sustaining mycobacterial physiology and survival. We would revise our statements in the paper to reflect the data. Results shown suggest that the tethering activity of the Nterminal region may contribute to mycobacterial morphology and survival. However, additional functions of this region can’t be ruled out. Similarly, the maintenance of lipid homeostasis by Wag31 may be associated with its tethering activity, although other mechanisms could also contribute to this process.
• Authors suggest that Wag31 acts as a scaffold for the IMD (Fig. 8). However, Meniche et. al. has shown that MurG as well as GlfT2, two well-characterized IMD proteins, do not colocalize with Wag31 (DivIVA) (https://doi.org/10.1073/pnas.1402158111). IMD proteins are always slightly subpolar while Wag31 is located to the tip of the cell. Therefore, the authors' biochemical data cannot be easily reconciled with microscopic observations in the literature. This raises a question regarding the validity of protein-protein interaction shown in Figure 7. Since this pull-down assay was conducted by mixing E. coli lysate expressing Wag31 and Msm lysate expression Wag31 interactors like MurG, it is possible that the interactions are not direct. Authors should interpret their data more cautiously. If authors cannot provide additional data and sufficient justifications, they should avoid proposing a confusing model like Figure 8 that contradicts published observations.
In the literature, MurG and GlfT2 have been shown to have polar localisation (Freeman et al., 2023; Hayashi et al., 2016; Kado et al., 2023) and two groups have shown slightly sub-polar localisation of MurG (García-Heredia et al., 2021; Meniche et al., 2014). Additionally, (Freeman et al., 2023) showed SepIVA to be a spatio-temporal regulator of MurG. MS/MS analysis of Wag31 immunoprecipitation data yielded both MurG and SepIVA to be interactors of Wag31 (Fig. 3). Given Wag31 also displays polar localisation, it is likely that it associates with the polar MurG. However, since a sub-polar localisation of MurG has also been reported, it is possible that they do not interact directly and another protein mediates their interaction. Based on the above, we will modify the model proposed in Fig. 8.
We agree that for validation of interaction, we performed pulldown experiments by mixing E. coli lysates expressing His-Wag31 full-length or truncated protein with M. smegmatis lysates expressing FLAG-tagged interacting proteins. The wash conditions used were quite stringent for these pull-down assays—the wash buffer contained 1% Triton X100 that eliminates all non-specific and indirect interactions. However, we agree that we cannot conclusively state that the interactions are direct without purifying the proteins and performing the experiment. We will describe this caveat in the revised manuscript and propose a model that reflects the results we obtained.
References:
Freeman, A. H., Tembiwa, K., Brenner, J. R., Chase, M. R., Fortune, S. M., Morita, Y. S., & Boutte, C. C. (2023). Arginine methylation sites on SepIVA help balance elongation and septation in Mycobacterium smegmatis. Mol Microbiol, 119(2), 208-223. https://doi.org/10.1111/mmi.15006
Garcia Fernandez, M. I., Ceccarelli, D., & Muscatello, U. (2004). Use of the fluorescent dye 10-N-nonyl acridine orange in quantitative and location assays of cardiolipin: a study on different experimental models. Anal Biochem, 328(2), 174-180. https://doi.org/10.1016/j.ab.2004.01.020
García-Heredia, A., Kado, T., Sein, C. E., Puffal, J., Osman, S. H., Judd, J., Gray, T. A., Morita, Y. S., & Siegrist, M. S. (2021). Membrane-partitioned cell wall synthesis in mycobacteria. eLife, 10. https://doi.org/10.7554/eLife.60263
Habibi Arejan, N., Ensinck, D., Diacovich, L., Patel, P. B., Quintanilla, S. Y., Emami Saleh, A., Gramajo, H., & Boutte, C. C. (2022). Polar protein Wag31 both activates and inhibits cell wall metabolism at the poles and septum. Front Microbiol, 13, 1085918. https://doi.org/10.3389/fmicb.2022.1085918
Hayashi, J. M., Luo, C. Y., Mayfield, J. A., Hsu, T., Fukuda, T., Walfield, A. L., Giffen, S. R., Leszyk, J. D., Baer, C. E., Bennion, O. T., Madduri, A., Shaffer, S. A., Aldridge, B. B., Sassetti, C. M., Sandler, S. J., Kinoshita, T., Moody, D. B., & Morita, Y. S. (2016). Spatially distinct and metabolically active membrane domain in mycobacteria. Proc Natl Acad Sci U S A, 113(19), 5400-5405. https://doi.org/10.1073/pnas.1525165113
Kado, T., Akbary, Z., Motooka, D., Sparks, I. L., Melzer, E. S., Nakamura, S., Rojas, E. R., Morita, Y. S., & Siegrist, M. S. (2023). A cell wall synthase accelerates plasma membrane partitioning in mycobacteria. eLife, 12, e81924. https://doi.org/10.7554/eLife.81924
Meniche, X., Otten, R., Siegrist, M. S., Baer, C. E., Murphy, K. C., Bertozzi, C. R., & Sassetti, C. M. (2014). Subpolar addition of new cell wall is directed by DivIVA in mycobacteria. Proc Natl Acad Sci U S A, 111(31), E32433251. https://doi.org/10.1073/pnas.1402158111
Mileykovskaya, E., & Dowhan, W. (2000). Visualization of phospholipid domains in Escherichia coli by using the cardiolipin-specific fluorescent dye 10-N-nonyl acridine orange. J Bacteriol, 182(4), 1172-1175. https://doi.org/10.1128/JB.182.4.1172-1175.2000
Petit, J. M., Maftah, A., Ratinaud, M. H., & Julien, R. (1992). 10N-nonyl acridine orange interacts with cardiolipin and allows the quantification of this phospholipid in isolated mitochondria. Eur J Biochem, 209(1), 267273. https://doi.org/10.1111/j.1432-1033.1992.tb17285.x
Renner, L. D., & Weibel, D. B. (2011). Cardiolipin microdomains localize to negatively curved regions of Escherichia coli membranes. Proc Natl Acad Sci U S A, 108(15), 6264-6269. https://doi.org/10.1073/pnas.1015757108
Schägger, H. (2006). Tricine-SDS-PAGE. Nat Protoc, 1(1), 16-22. https://doi.org/10.1038/nprot.2006.4
Xu, W. X., Zhang, L., Mai, J. T., Peng, R. C., Yang, E. Z., Peng, C., & Wang, H. H. (2014). The Wag31 protein interacts with AccA3 and coordinates cell wall lipid permeability and lipophilic drug resistance in Mycobacterium smegmatis. Biochem Biophys Res Commun, 448(3), 255-260. https://doi.org/10.1016/j.bbrc.2014.04.116
Recommendations for the authors:
Reviewer #1 (Recommendations for the authors):
(1) Ln 130. A better clarification/discussion is required here. It is clear that both depletion and overexpression have an effect in levels of various lipids, but subsequent descriptions show that they affect different classes of lipids.
We thank the reviewer for the comment. We have included a clarification for this in the discussion section.
(2) The pulldown assays results are interesting, but the links are tentative.
We thank the reviewer for the comment. The interactome of Wag31 was identified through the immunoprecipitation of Flag-tagged Wag31 complemented at an integrative locus in Wag31 mutant background to avoid overexpression artifacts. We used Msm::gfp expressing an integrative copy (at L5 locus) of FLAG-GFP as a control to subtract non-specific interactions. The experiment was performed in biological triplicates, and interactors that appeared in all replicates were selected for further analysis. Although we identified more than 100 interactors of Wag31, we analyzed only the top 25 hits, with a PSM cut-off 18 and unique peptides5. Additionally, two of Wag31's established interactors, AccD5 and Rne, were among the top five hits, thus validating our data.
Though we agree that the interactions can either be direct or through a third partner, the fact that we obtained known interactors of Wag31 makes us believe these interactions are genuine. Moreover, for validation, we performed pulldown experiments by mixing E. coli lysates expressing HisWag31 full-length or truncated protein with M. smegmatis lysates expressing FLAG-tagged interacting proteins. The wash conditions used were quite stringent for these pull-down assays—the wash buffer contained 1% Triton X100 that eliminates all non-specific and indirect interactions. However, we agree that we cannot conclusively state that the interactions are direct without purifying the proteins and performing the experiment. We will describe this caveat in the revised manuscript.
(3) The authors may perhaps like to rephrase claims of effects lipid homeostasis, as my understanding is that lipid localisation rather than catabolism/breakdown is affected.
We thank the reviewer for the comment. In this manuscript, we are trying to convey that Wag31 is a spatiotemporal regulator of lipid metabolism. It is a peripheral protein that is hooked to the membrane via Cardiolipin and forms a scaffold at the poles, which helps localize several enzymes involved in lipid metabolism.
Homeostasis is the process by which an organism maintains a steady-state of balance and stability in response to changes. Depletion of Wag31 not only results in delocalisation of lipids in intracellular lipid inclusions but also leads to changes in the levels of various lipid classes. Advancement in the field of spatial biology underscores the importance of native localization of various biological molecules crucial for maintaining a steady-cell of the cell. Hence, we have used the word “homeostasis” to describe both the changes observed in lipid metabolism.
Reviewer #2 (Recommendations for the authors):
I recommend the following experiments to strengthen the data presented:
(1) Include a non-interacting FLAG-tagged protein as a negative control in the pull-down experiment to strengthen this data.
We thank the reviewer for the comment. As suggested, we have included non-interacting FLAGtagged proteins as negative controls in the pulldown experiment. We chose MmpL4 and MmpS5 which were not found in the Wag31 interactome data. We performed pull-down experiments with both of them and included an interactor of Wag31 i.e. Msm2092 as a positive control. Fig. S3b revised shows E. coli lysate expressing His-Wag31 which was incubated with Msm lysates expressing either FLAG taggedMmpL4 or -MmpS5 or -Msm2092 (Fig. S3c revised). The mixed lysates were pulled down with Cobalt beads that bind to the His-tagged protein and analysed using Western blot analysis by probing with anti-FLAG antibody. The pull down experiments were performed independently twice, every time with Msm2092 as the positive control (Fig. S3d. revised).
(2) Perform the pull-down experiments using only the Wag31 N-terminus to rule out any role that it may have in the protein-protein interactions.
We thank the reviewer for the comment. To rule out the possibility of N-terminal of Wag31 in mediating protein-protein interactions, we cloned the N-terminal of Wag31 that comprises the DivIVAdomain in pET28b vector (Fig. 7a revised). Subsequently, the truncated protein, hereafter called Wag31<sub>∆C</sub> flanked by 6X His tags at both the termini was expressed in E. coli and subsequently mixed with Msm lysates expressing interactors of Wag31 (Fig. 7b-c revised). Earlier experiments with Wag31<sub>∆1-60</sub> or Wag31<sub>∆N</sub> were performed with MurG, SepIVA, Msm2092 and AccA3 (Fig. 7 previous) so we used the same set of interactors to test our hypothesis. Briefly, His-Wag31<sub>∆C</sub>was mixed with Msm lysates expressing either FLAG-MurG, -SepIVA, -Msm2092 or -AccA3 and pull down experiments were performed as described previously. FLAG-MmpS5, a non-interactor of Wag31 was used as a negative control. As shown in Fig. 7d revised, His-Wag31 could bind to all the four interactors whereas His-Wag31<sub>∆C</sub> couldn’t, strengthening the conclusion that interactions of Wag31 with other proteins are mediated by its C-terminal. However, we can’t ignore the possibility of other proteins binding to the Nterminal of Wag31. Unfortunately, due to poor expression/instability of Wag31<sub>∆C</sub> in mycobacterial shuttle vectors, we couldn’t perform a global interactome analysis of Wag31<sub>∆C</sub>.
Minor comments:
- Please check the legend of Fig. 1g, it appears to be labelled incorrectly.
We have checked it. It is correct. From Fig. 1g we are trying to reflect on the percentages of cells of the three strains i.e. Msm+ATc, Δwag31-ATc, and Δwag31+ATc displaying rod, round or bulged morphology.
- For MS/MS analysis, a GFP control is mentioned but it is not indicated how this was incorporated in the data analysis. This information should be added.
We have incorporated that in the revised methodology.
- The information presented in Fig. 3a, e and f could be combined in one table.
We appreciate the idea of the reviewer but we prefer a pictorial representation of the data. It allows readers to consume the information in parts, make quicker comparisons and understand trends easily.
- Fig. 4c Wag31K20A appears smaller in size than the wild-type protein - why is this the case? Is this not a single amino acid substitution?
Though K20A is a single amino acid substitution, it alters the mobility of Wag31 on SDS-PAGE gel. The sequence analysis of the plasmid expressing Wag31<sub>K20A</sub> doesn’t show additional mutations other than the desired K20A. The change in mobility could be due to a change in the conformation of Wag31<sub>K20A</sub> or its ability to bind to SDS or both that modify its mobility under the influence of electric field.
- Please clarify what is contained in the first panel of fig 4e. compared to what is in the second panel.
The first panel represents CL-Dil-Liposomes before incubation with Wag31-GFP and the second panel shows CL-Dil-Liposomes after incubation with Wag31-GFP. The third panel shows the mixture as observed in the green channel to investigate the localisation of Wag31-GFP in the liposome-protein mix. Fourth panel shows the merged of second and third.
- The data in Fig 6d suggests higher levels of CL in the ∆wag31 compared to wild-type - how do the authors reconcile this with the MS data in Fig. 2g showing lower CL levels?
Fig. 6d represents the distribution of CL localisation in the tested strains of mycobacteria whereas Fig. 2g shows the absolute levels of CL in various strains. We attribute greater confidence on the lipidomics data which suggests down regulation of CL species. The NAO staining and microscopy is merely for studying localization of the CL along the cell, and cannot be used to reliably quantify or equate it to CL levels. The staining using a probe such as NAO is dependent on factors such as hydrophobicity and permeability of the cell wall, which we expect to be severely altered in a Wag31 mutant. Therefore, the increased staining of NAO seen in Wag31 mutant could just be reflective of the increased uptake of the dye rather than absolute levels of CL. The specificity of staining and localization however can be expected to be unaltered.
Reviewer #3 (Recommendations for the authors):
Following are suggestions for improving the writing and presentation.
• Figure 1, the meaning of the yellow arrows present in f and h should be mentioned in the figure legend.
We have incorporated that in the revised legend. In Fig.1f, the yellow arrowhead represents the bulged pole morphology whereas in Fig. 1h, it indicates intracellular lipid inclusions.
• Figure 7 legend refers to panels g, h, and i. However, Figure 7 only has panels a-c. The legend lacks a description of panel c.
We have corrected the typos and the legend.
• Figure S1, F2-R2 and F3-R3 expected sizes should be stated in the legend of the figure.
We have updated the legends.
• Figure S5, is this the same figure as 5e? If so, there is no need for this figure.
We have removed Fig. S5.
• Methods need to be written more carefully with enough details. I listed some of the concerns below.
Detailed methodology was previously provided in the supplementary material and now we have moved it to the materials and methods in the revised manuscript.
• Line 392, provide more details on western blotting. What is the secondary antibody? What image documentation system was used?
We have updated the methodology.
• Line 400, while the methods may be the same as the reference 64, authors should still provide key details such as the way samples were fixed and processed for SEM and TEM.
We have provided a detailed description of the same in methodology in the revised version.
• Line 437, how do authors calculate the concentration of liposome to be 10 µM? Do they possibly mean the concentration of phospholipids used to make the liposomes?
Yes, this is the concentration of total lipids used to make liposomes. 1 μM of Wag31 or its mutants were mixed with 100 nm extruded liposomes containing 10 μm total lipid in separate Eppendorf tubes.
• Supplemental Line 9, "turns of" should read "turns off".
We have edited this.
• Supplemental Line 13, define LHS and RHS.
LHS or left hand sequence and RHS or right hand sequence refers to the upstream and downstream flanking regions of the gene of interest.
• Supplemental Line 20, indicate the manufacturer of the microscope and type of the objective lens.
We have added these details now.
• Supplemental Line 31, define MeOH, or use a chemical formula like chloroform.
MeOH is methanol. We have provided a chemical formula in the revised version.
• Supplemental Line 53, indicate the concentration of trypsin.
We have included that in the revised version.
• Supplemental Line 72, g is not a unit. "30,000 g" should be "30,000x g".
We have revised this in the manuscript.
• Supplemental Line 114, provide more details on western blotting. What is the manufacturer of antiFLAG antibody? What is the secondary antibody? How was the antibody binding visualized? What image documentation system was used?
We have provided these details in the revised version.
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agrigenre.hypotheses.org agrigenre.hypotheses.org
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www.biorxiv.org www.biorxiv.org
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eLife Assessment
The authors provide valuable insights into the candidate upstream transcriptional regulatory factors that control the spatiotemporal expression of selector genes and their targets for GABAergic vs glutamatergic neuron fate in the anterior brainstem. The computational analysis of single-cell RNA-seq and single-cell ATAC-seq datasets to predict TF binding combined with cut and tag-seq to find TF binding represents a solid approach to support the findings in the study, although the display and discussion of the datasets could be strengthened. This study will be of interest to neurobiologists who study transcriptional mechanisms of neuronal differentiation.
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Reviewer #1 (Public review):
Summary:
The objective of this research is to understand how the expression of key selector transcription factors, Tal1, Gata2, Gata3, involved in GABAergic vs glutamatergic neuron fate from a single anterior hindbrain progenitor domain is transcriptionally controlled. With suitable scRNAseq, scATAC-seq, CUT&TAG, and footprinting datasets, the authors use an extensive set of computational approaches to identify putative regulatory elements and upstream transcription factors that may control selector TF expression. This data-rich study will be a valuable resource for future hypothesis testing, through perturbation approaches, of the many putative regulators identified in the study. The data are displayed in some of the main and supplemental figures in a way that makes it difficult to appreciate and understand the authors' presentation and interpretation of the data in the Results narrative. Primary images used for studying the timing and coexpression of putative upstream regulators, Insm1, E2f1, Ebf1, and Tead2 with Tal1 are difficult to interpret and do not convincingly support the authors' conclusions. There appears to be little overlap in the fluorescent labeling, and it is not clear whether the signals are located in the cell soma nucleus.
Strengths:
The main strength is that it is a data-rich compilation of putative upstream regulators of selector TFs that control GABAergic vs glutamatergic neuron fates in the brainstem. This resource now enables future perturbation-based hypothesis testing of the gene regulatory networks that help to build brain circuitry.
Weaknesses:
Some of the findings could be better displayed and discussed.
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Author response:
Reviewer #1 (Public review):
Summary:
The objective of this research is to understand how the expression of key selector transcription factors, Tal1, Gata2, Gata3, involved in GABAergic vs glutamatergic neuron fate from a single anterior hindbrain progenitor domain is transcriptionally controlled. With suitable scRNAseq, scATAC-seq, CUT&TAG, and footprinting datasets, the authors use an extensive set of computational approaches to identify putative regulatory elements and upstream transcription factors that may control selector TF expression. This data-rich study will be a valuable resource for future hypothesis testing, through perturbation approaches, of the many putative regulators identified in the study. The data are displayed in some of the main and supplemental figures in a way that makes it difficult to appreciate and understand the authors' presentation and interpretation of the data in the Results narrative. Primary images used for studying the timing and coexpression of putative upstream regulators, Insm1, E2f1, Ebf1, and Tead2 with Tal1 are difficult to interpret and do not convincingly support the authors' conclusions. There appears to be little overlap in the fluorescent labeling, and it is not clear whether the signals are located in the cell soma nucleus.
Strengths:
The main strength is that it is a data-rich compilation of putative upstream regulators of selector TFs that control GABAergic vs glutamatergic neuron fates in the brainstem. This resource now enables future perturbation-based hypothesis testing of the gene regulatory networks that help to build brain circuitry.
We thank Reviewer #1 for the thoughtful assessment and recognition of the extensive datasets and computational approaches employed in our study. We appreciate the acknowledgment that our efforts in compiling data-rich resources for identifying putative regulators of key selector transcription factors (TFs)—Tal1, Gata2, and Gata3—are valuable for future hypothesis-driven research.
Weaknesses:
Some of the findings could be better displayed and discussed.
We acknowledge the concerns raised regarding the clarity and interpretability of certain figures, particularly those related to expression analyses of candidate upstream regulators such as Insm1, E2f1, Ebf1, and Tead2 in relation to Tal1. We agree that clearer visualization and improved annotation of fluorescence signals are crucial to accurately support our conclusions. In our revised manuscript, we will enhance image clarity and clearly indicate sites of co-expression for Tal1 and its putative regulators, ensuring the results are more readily interpretable. Additionally, we will expand explanatory narratives within the figure legends to better align the figures with the results section.
Reviewer #2 (Public review):
Summary:
In the manuscript, the authors seek to discover putative gene regulatory interactions underlying the lineage bifurcation process of neural progenitor cells in the embryonic mouse anterior brainstem into GABAergic and glutamatergic neuronal subtypes. The authors analyze single-cell RNA-seq and single-cell ATAC-seq datasets derived from the ventral rhombomere 1 of embryonic mouse brainstems to annotate cell types and make predictions or where TFs bind upstream and downstream of the effector TFs using computational methods. They add data on the genomic distributions of some of the key transcription factors and layer these onto the single-cell data to get a sense of the transcriptional dynamics.
Strengths:
The authors use a well-defined fate decision point from brainstem progenitors that can make two very different kinds of neurons. They already know the key TFs for selecting the neuronal type from genetic studies, so they focus their gene regulatory analysis squarely on the mechanisms that are immediately upstream and downstream of these key factors. The authors use a combination of single-cell and bulk sequencing data, prediction and validation, and computation.
We also appreciate the thoughtful comments from Reviewer #2, highlighting the strengths of our approach in elucidating gene regulatory interactions that govern neuronal fate decisions in the embryonic mouse brainstem. We are pleased that our focus on a critical cell-fate decision point and the integration of diverse data modalities, combined with computational analyses, has been recognized as a key strength.
Weaknesses:
The study generates a lot of data about transcription factor binding sites, both predicted and validated, but the data are substantially descriptive. It remains challenging to understand how the integration of all these different TFs works together to switch terminal programs on and off.
Reviewer #2 correctly points out that while our study provides extensive data on predicted and validated transcription factor binding sites, clearly illustrating how these factors collectively interact to regulate terminal neuronal differentiation programs remains challenging. We acknowledge the inherently descriptive nature of the current interpretation of our combined datasets.
In our revision, we will clarify how the different data types support and corroborate one another, highlighting what we consider the most reliable observations of TF activity. Additionally, we will revise the discussion to address the challenges associated with interpreting the highly complex networks of interactions within the gene regulatory landscape.
We sincerely thank both reviewers for their constructive feedback, which we believe will significantly enhance the quality and accessibility of our manuscript.
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social-media-ethics-automation.github.io social-media-ethics-automation.github.io
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W3Schools. Introduction to HTML. URL: https://www.w3schools.com/html/html_intro.asp (visited on 2023-11-24).
The W3Schools HTML Introduction page explains that HTML is the basic language used to build web pages. It talks about how HTML uses tags (like labels) to mark things like titles, headings, and paragraphs. For example, you use one tag type to create a heading and another for a paragraph. It even shows a simple example of what a basic web page looks like in code. It also mentions that your web browser (like Chrome or Safari) reads this code and turns it into the websites you see. And there’s a special line at the top of the page that helps the browser understand it’s working with HTML.
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uo.unisa.edu.au uo.unisa.edu.au
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Add a Page Note with the tag Welcome to let us know you've joined.
Welcome.
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download, instrumental hip-hop,
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pop, download, popmusic,
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gangsta, rap, download,
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funk, download,
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learn.cantrill.io learn.cantrill.io
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Welcome back and this is going to be a super quick lesson where I just want to discuss cost allocation tags. So this is something you'll use in normal operations when you manage AWS accounts. But for the exam, there are a number of key points that you need to be aware of. So let's keep this brief and just jump in and get started.
Cost allocation tags are things that you can enable to provide additional information for any billing reports available within AWS. So cost allocation tags need to be enabled individually. And this is either on a per account basis for standard accounts or something that's performed in the organizational master account if you use AWS Organizations.
Now cost allocation tags come in two different forms. You have AWS generated ones. You can always start with AWS: and two very common ones are AWS:createdBy or AWS:cloudformation:stack-name. And if you enable cost allocation tags, then these tags are added to AWS resources automatically by AWS.
Now I always see questions in the exam which do mention AWS:createdBy. Now this details which identity created a resource as long as cost allocation tags are enabled. So this is not something that can be added retroactively. You need to make sure that this is enabled on an account or for an organization. And from that point onward, AWS will automatically add this cost allocation tag to any resource or any supported resource within the account.
There are also user defined tags which can be enabled. So you can create these—for example, maybe you wanted to have department tags or cost center tags or tags that indicated whether environments were production or development. And you can enable these and use them as cost allocation tags and these will be visible in any AWS cost reporting.
Now both of these—so user defined and AWS defined or AWS generated—they're going to be visible once enabled within AWS cost reports and these can be used as a filter. So you're able to determine which resources were created by a user or which resources belong to certain departments or cost centers. And you can use this as part of your organizational finance systems to correctly allocate AWS costs to specific areas of your business.
Now enabling these and having them so they're visible within cost reports can take up to 24 hours. So this is something that you need to plan in advance. None of these are retroactive. So keep that in mind for the exam and real world usage.
Now to illustrate how this works and what better way than to use some obnoxiously large graphics. Let's take a simple example: two EC2 instances for the category application. Let's say that in advance I create or enable two different cost allocation tags, AWS:createdBy and a user defined tag called app. This is what you might see.
Resources created will automatically be tagged with these two different tags. So the AWS generated AWS:createdBy tag, which allows you to see which identity created that resource. And then the user defined tag user:application and the two different current values for this tag are Categorim-prod and Categorim-dev.
Now any reporting which is generated from this point onward will include these tags. So we could split out the costs for our finance team detailing which costs are allocated for the Categorim production and the Categorim development application. And then we could also produce isolated costs for resources created by specific AWS users.
So by using cost allocation tags effectively, we can feed these costs into our organizational finance processes.
Now that's pretty much all you need to know for the exam. Just the format of these tags—pay specific attention to AWS:createdBy because that's what I see in the exam all the time. Just know that these need to be enabled. They are not retroactive. And once you've enabled them, it can take up to 24 hours for these to be visible and used by AWS.
So that being said, that's everything I wanted to cover in this lesson. Go ahead and complete the video. And when you're ready, I'll look forward to you joining me in the next.
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docdrop.org docdrop.orgview1
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In the past three decades, moreover, as the class gaps have rapidly widened, local property taxes in many states have funded a smaller and smaller fraction of school budgets, in part because court decisions in those states have mandated equalization of spending across school districts.
This is connected to opportunity hoarding, where affluent families secure exclusive advantages like AP courses, test prep, legacy admissions, and extracurricular stacking, that limit mobility for others. Low-income high achievers are disproportionately underrepresented at selective institutions, due not to ability, but to a lack of information and institutional support. I applied to college on my own. No guidance counselor explained FAFSA, CA Dreamer, or TAG to me because there were none. I missed some early deadlines because I didn’t know they existed. The most ironic thing was that my friends and posts from Reddit helped me to submit my college application.
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www.biorxiv.org www.biorxiv.org
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Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.
Learn more at Review Commons
Reply to the reviewers
Manuscript number: RC-2024-02465
Corresponding author(s): Saravanan, Palani
1. General Statements
We would like to thank the Review Commons Team for handling our manuscript and the Reviewers for their constructive feedback and suggestions. In our revised manuscript, we have addressed and incorporated all the major suggestions of the reviewers, and we have also added new significant data on the role of Tropomyosin in regulation of endocytosis through its control over actin monomer pool maintenance and actin network homeostasis. We believe that with all these additions, our study has significantly gained in quality, strength of conclusions made, and scope for future work.
2. Point-by-point description of the revisions
Reviewer #1
Evidence, reproducibility and clarity
There are 2 Major issues -
Having an -ala-ser- linker between the GFP and tropomyosin mimics acetylation. This is not the case, and more likely the this linker acts as a spacer that allows tropomyosin polymers to form on the actin, and without it there is steric hindrance. A similar result would be seen with a simple flexible uncharged linker. It has been shown in a number of labs that the GFP itself masks the effect of the charge on the amino terminal methionine. This is consistent with NMR, crystallographic and cryo structural studies. Biochemical studies should be presented to demonstrate that the impact of a linker for the conclusions stated to be made, which provide the basis of a major part of this study.
Response: We would like to clarify that all mNG-Tpm constructs used in our study contain a 40 amino-acid (aa) flexible linker between the N-terminal mNG fluorescent protein and the Tpm protein as per our earlier published study (Hatano et al., 2022). During initial optimization, we have also experimented with linker length and the 40aa-linker length works optimally for clear visualization of Tpm onto actin cable structures in budding yeast, fission yeast (both S. pombe and S. japonicus), and mammalian cells (Hatano et al., 2022). These constructs have also been used since in other studies (Wirshing et al., 2023; Wirshing and Goode, 2024) and currently represents the best possible strategy to visualize Tpm isoforms in live cells. In our study, we characterized these proteins for functionality and found that both mNG-Tpm1 and mNG-Tpm2 were functional and can rescue the synthetic lethality observed in Dtpm1Dtpm2 cells. During our study, we observed that mNG-Tpm1 expression from a single-copy integration vector did not restore full length actin cables in Dtpm1 cells (Fig. 1B, 1C). We hypothesized that this could be a result of reduced binding affinity of the tagged tropomyosin due to lack of normal N-terminal acetylation which stabilizes the N-terminus. The 40aa linker is unstructured and may not be able to neutralize the charge on the N-terminal Methionine, thus, we tried to insert -Ala-Ser- dipeptide which has been routinely used in vitro biochemical studies to stabilize the N-terminal helix and impart a similar effect as the N-terminal acetylation (Alioto et al., 2016; Palani et al., 2019; Christensen et al., 2017) by restoring normal binding affinity of Tpm to F-actin (Monteiro et al., 1994; Greenfield et al., 1994). We observed that addition of the -Ala-Ser- dipeptide to mNG-Tpm fusion, indeed, restored full length actin cables when expressed in Dtpm1 cells, performing significantly better in our in vivo experiments (Fig. 1B, 1C). We agree with the reviewer that the -AS- dipeptide addition may not mimic N-terminal acetylation structurally but as per previous studies, it may stabilize the N-terminus of Tpm and allow normal head-to-tail dimer formation (Greenfield et al., 1994; Monteiro et al., 1994; Frye et al., 2010). We have discussed this in our new Discussion section (Lines 350-372). Since, the addition of -AS- dipeptide was referred to as "acetyl-mimic (am)" in a previous study (Alioto et al., 2016), we continued to use the same nomenclature in our study. Now as per your suggestions and to be more accurate, we have renamed "mNG-amTpm" constructs as "mNG-ASTpm" throughout the study to not confuse or claim that -AS- addition mimics acetylation. In any case, we have not seen any other ill effect of -AS- dipeptide introduction in addition to our 40 amino acid linker suggesting that it can also be considered part of the linker. Although, we agree with the reviewer that biochemical characterization of the effect of linker would be important to determine, we strongly believe that it is currently outside the scope of this study and should be taken up for future work with these proteins. Our study has majorly aimed to understand the functionality and utility of these mNG-Tpm fusion proteins for cell biological experiments in vivo, which was not done earlier in any other model system.
My major issue however is making the conclusions stated here, using an amino-terminal fluorescent protein tag that s likely to impact any type of isoform selection at the end of the actin polymer. Carboxyl terminal tagging may have a reduced effect, but modifying the ends of the tropomyosin, which are integral in stabilising end to end interactions with itself on the actin filament, never mind any section systems that may/maynot be present in the cell, is not appropriate.
Response: We agree with the reviewer that N-terminal tagging of tropomyosin may have effects on its function, but these constructs represent the only fluorescently tagged functional tropomyosin constructs available currently while C-terminal fusions are either non-functional (we were unable to construct strains with endogenous Tpm1 gene fused C-terminally to GFP) or do not localize clearly to actin structures (See Figure R1 showing endogenous C-terminally tagged Tpm2-yeGFP that shows almost no localization to actin cables). To our knowledge, our study represents a first effort to understand the question of spatial sorting of Tpm isoforms, Tpm1 and Tpm2, in S. cerevisiae and any future developments with better visualization strategies for Tpm isoforms without compromising native N-terminal modifications and function will help improve our understanding of these proteins in vivo. We have also discussed these possibilities in our new Discussion section (Lines 391-396).
Significance
This paper explores the role of formin in determining the localisation of different tropomyosins to different actin polymers and cellular locations within budding yeast. Previous studies have indicated a role for the actin nucleating proteins in recruiting different forms of tropomyosin within fission yeast. In mammalian cells there is variation in the role of formins in affiecting tropomyosin localisation - variation between cell type. There is also evidence that other actin binding proteins, and tropomyosin abundance play roles in regulating the tropomyosin-actin association according to cell type. Biochemical studies have previously been undertaken using budding yeast and fission yeast that the core actin polymerisation domain of formins do not interact with tropomyosin directly. The significance of this study, given the above, and the concerns raised is not clear to this reviewer.
Response: __Our study explores multiple facets of Tropomyosin (Tpm) biology. The lack of functional tagged Tpm has been a major bottleneck in understanding Tpm isoform diversity and function across eukaryotes. In our study, we characterize the first functional tagged Tpm proteins (Fig. 1, Fig. S1) and use them to answer long-standing questions about localization and spatial sorting of Tpm isoforms in the model organism S. cerevisiae (Fig. 2, Fig. 3, Fig. S2, Fig. S3). We also discover that the dual Tpm isoforms, Tpm1 and Tpm2, are functionally redundant for actin cable organization and function, while having gained divergent functions in Retrograde Actin Cable Flow (RACF) (Fig. 4, Fig. 5A-D, Fig. S4, Fig. S5, Fig. S6). We have now added new data on role of global Tpm levels controlling endocytosis via maintenance of normal linear-to-branched actin network homeostasis in S. cerevisiae (Fig. 5E-G)__. We respectfully differ with the reviewer on their assessment of our study and request the reviewer to read our revised manuscript which discusses the significance, limitations, and future perspectives of our study in detail.
Reviewer #2
Evidence, reproducibility and clarity
This manuscript by Dhar, Bagyashree, Palani and colleagues examines the function of the two tropomyosins, Tpm1 and Tpm2, in the budding yeast S. cerevisiae. Previous work had shown that deletion of tpm1 and tpm2 causes synthetic lethality, indicating overlapping function, but also proposed that the two tropomyosins have distinct functions, based on the observation that strong overexpression of Tpm2 causes defects in bud placement and fails to rescue tpm1∆ phenotypes (Drees et al, JCB 1995). The manuscript first describes very functional mNeonGreen tagged version of Tpm1 and Tpm2, where an alanine-serine dipeptide is inserted before the first methionine to mimic acetylation. It then proposes that the Tpm1 and Tpm2 exhibit indistinguishable localization and that low level overexpression (?) of Tpm2 can replace Tpm1 for stabilization of actin cables and cell polarization, suggesting almost completely redundant functions. They also propose on specific function of Tpm2 in regulating retrograde actin cable flow.
Overall, the data are very clean, well presented and quantified, but in several places are not fully convincing of the claims. Because the claims that Tpm1 and Tpm2 have largely overlapping function and localization are in contradiction to previous publication in S. cerevisiae and also different from data published in other organisms, it is important to consolidate them. There are fairly simple experiments that should be done to consolidate the claims of indistinguishable localization, and levels of expression, for which the authors have excellent reagents at their disposal.
1. Functionality of the acetyl-mimic tagged tropomyosin constructs: The overall very good functionality of the tagged Tpm constructs is convincing, but the authors should be more accurate in their description, as their data show that they are not perfectly functional. For instance, the use of "completely functional" in the discussion is excessive. In the results, the statement that mNG-Tpm1 expression restores normal growth (page 3, line 69) is inaccurate. Fig S1C shows that tpm1∆ cells expressing mNG-Tpm1 grow more slowly than WT cells. (The next part of the same sentence, stating it only partially restores length of actin cables should cite only Fig S1E, not S1F.) Similarly, the growth curve in Fig S1C suggests that mNG-amTpm1, while better than mNG-Tpm1 does not fully restore the growth defect observed in tpm1∆ (in contrast to what is stated on p. 4 line 81). A more stringent test of functionality would be to probe whether mNG-amTpm1 can rescue the synthetic lethality of the tpm1∆ tpm2∆ double mutant, which would also allow to test the functionality of mNG-amTpm2.
__Response: __We would like to thank the reviewer for his feedback and suggestions. Based on the suggestions, we have now more accurately described the growth rescue observed by expression of mNG-ASTpm1 in Dtpm1 cells in the revised text. We have also removed the use of "completely functional" to describe mNG-Tpm functionality and corrected any errors in Figure citations in the revised manuscript.
As per reviewers' suggestion, we have now tested rescue of synthetic lethality of Dtpm1Dtpm2 cells by expression of all mNG-Tpm variants and we find that all of them are capable of restoring the viability of Dtpm1Dtpm2 cells when expressed under their native promoters via a high-copy plasmid (pRS425) (Fig. S1E) but only mNG-Tpm1 and mNG-ASTpm1 restored viability of Dtpm1Dtpm2 cells when expressed under their native promoters via an integration plasmid (pRS305) (Fig. S1F). These results clearly suggest that while both mNG-Tpm1 and mNG-Tpm2 constructs are functional, Tpm1 tolerates the presence of the N-terminal fluorescent tag better than Tpm2. These observations now enhance our understanding of the functionality of these mNG-Tpm fusion proteins and will be a useful resource for their usage and experimental design in future studies in vivo.
It would also be nice to comment on whether the mNG-amTpm constructs really mimicking acetylation. Given the Ala-Ser peptide ahead of the starting Met is linked N-terminally to mNG, it is not immediately clear it will have the same effect as a free acetyl group decorating the N-terminal Met.
Response: __We agree with the reviewer's observation and for the sake of clarity and accuracy, we have now renamed "mNG-amTpm" with "mNG-ASTpm". The use of -AS- dipeptide is very routine in studies with Tpm (Alioto et al., 2016; Palani et al., 2019; Christensen et al., 2017) and its addition restores normal binding affinities to Tpm proteins purified from E. coli (Monteiro et al., 1994). We agree with the reviewer that the -AS- dipeptide addition may not mimic N-terminal acetylation structurally but as per previous studies, it may help neutralize the impact of a freely protonated Met on the alpha-helical structure and stabilize the N-terminus helix of Tpm and allow normal head-to-tail dimer formation (Monteiro et al., 1994; Frye et al., 2010; Greenfield et al., 1994). Consistent with this, we also observe a highly significant improvement in actin cable length when expressing mNG-ASTpm as compared to mNG-Tpm in Dtpm1 cells, suggesting an improvement in function probably due to increased binding affinity (Fig. 1B, 1C). We have also discussed this in our answer to Question 1 of Reviewer 1 and the revised manuscript (Lines 350-372)__.
__ Localization of Tpm1 and Tpm2:__Given the claimed full functionality of mNG-amTpm constructs and the conclusion from this section of the paper that relative local concentrations may be the major factor in determining tropomyosin localization to actin filament networks, I am concerned that the analysis of localization was done in strains expressing the mNG-amTpm construct in addition to the endogenous untagged genes. (This is not expressly stated in the manuscript, but it is my understanding from reading the strain list.) This means that there is a roughly two-fold overexpression of either tropomyosin, which may affect localization. A comparison of localization in strains where the tagged copy is the sole Tpm1 (respectively Tpm2) source would be much more conclusive. This is important as the results are making a claim in opposition to previous work and observation in other organisms.
Response: __We thank the reviewer for this observation and their suggestions. We agree that relative concentrations of functional Tpm1 and Tpm2 in cells may influence the extent of their localizations. As per the reviewer's suggestion, we have now conducted our quantitative analysis in cells lacking endogenous Tpm1 and only expressing mNG-ASTpm1 from an integrated plasmid copy at the leu2 locus and the data is presented in new __Figure S3. We compared Tpm-bound cable length (Fig. S3A, S3B) __and Tpm-bound cable number (Fig. S3A, S3C) along with actin cable length (Fig. S3D, S3E) and actin cable number (Fig. S3D, S3F) in wildtype, Dbnr1, and Dbni1 cells. Our analysis revealed that mNG-ASTpm1 localized to actin cable structures in wildtype, Dbnr1, and Dbni1 cells and the decrease observed in Tpm-bound cable length and number upon loss of either Bnr1 or Bni1, was accompanied by a corresponding decrease in actin cable length and number upon loss of either Bnr1 or Bni1. Thus, this analysis reached the same conclusion as our earlier analysis (Fig. 2) that mNG-ASTpm1 does not show preference between Bnr1 and Bni1-made actin cables. mNG-ASTpm2 did not restore functionality, when expressed as single integrated copy, in Dtpm1Dtpm2 cells (new results in __Fig. S1E, S1F, S5A) thus, we could not conduct a similar analysis for mNG-ASTpm2. This suggests that use of mNG-ASTpm2 would be more meaningful in the presence of endogenous Tpm2 as previously done in Fig. 2D-F.
We have now also performed additional yeast mating experiments with cells lacking bnr1 gene and expressing either mNG-ASTpm1 or mNG-ASTpm2 and the data is shown in new Figure 3. From these observations, we observe that both mNG-ASTpm1 and mNG-ASTpm2 localize to the mating fusion focus in a Bnr1-independent manner (Fig. 3B, 3D) and suggests that they bind to Bni1-made actin cables that are involved in polarized growth of the mating projection. These results also add strength to our conclusion that Tpm1 and Tpm2 localize to actin cables irrespective of which formin nucleates them. Overall, these new results highlight and reiterate our model of formin-isoform independent binding of Tpm1 and Tpm2 in S. cerevisiae.
In fact, although the authors conclude that the tropomyosins do not exhibit preference for certain actin structures, in the images shown in Fig 2A and 2D, there seems to be a clear bias for Tpm1 to decorate cables preferentially in the bud, while Tpm2 appears to decorate them more in the mother cell. Is that a bias of these chosen images, or does this reflect a more general trend? A quantification of relative fluorescence levels in bud/mother may be indicative.
Response: __We thank the reviewer for pointing this out. Our data and analysis do not suggest that Tpm1 and Tpm2 show any preference for decoration of cables in either mother or bud compartment. As per the reviewer's suggestion, we have now quantified the ratio of mean mNG fluorescence in the bud to the mother (Bud/Mother) and the data is shown in __Figure. S2G. The bud-to-mother ratio was similar for mNG-ASTpm1 and mNG-ASTpm2 in wildtype cells, and the ratio increased in Dbnr1 cells and decreased in Dbni1 cells for both mNG-ASTpm1 and mNG-ASTpm2 (Fig. S2G). __This is consistent with the decreased actin cable signal in the mother compartment in Dbnr1 cells and decreased actin cable signal in the bud compartment in Dbni1 cells (Fig. S2A-D). Thus, our new analysis shows that both mNG-ASTpm1 and mNG-ASTpm2 have similar changes in their concentration (mean fluorescence) upon loss of either formins Bnr1 and Bni1 and show similar ratios in wildtype cells as well, suggesting no preference for binding to actin cables in either bud or mother compartment. The preference inferred by the reviewer seems to be a bias of the current representative images and thus, we have replaced the images in __Fig. 2A, 2D to more accurately represent the population.
The difficulty in preserving mNG-amTpm after fixation means that authors could not quantify relative Tpm/actin cable directly in single fixed cells. Did they try to label actin cables with Lifeact instead of using phalloidin, and thus perform the analysis in live cells?
__Response: __We did not use LifeAct for our analysis as LifeAct is known to cause expression-dependent artefacts in cells (Courtemanche et al., 2016; Flores et al., 2019; Xu and Du, 2021) and it also competes with proteins that regulate normal cable organization like cofilin. Use of LifeAct would necessitate standardization of expression to avoid such artefacts in vivo. Also, phalloidin staining provides the best staining of actin cables and allows for better quantitative results in our experiments. The use of LifeAct along with mNG-Tpm would also require optimization with a red fluorescent protein which usually tend to have lower brightness and photostability. However, during the revision of our study, a new study from Prof. Goode's lab has developed and optimized expression of new LifeAct-3xmNeonGreen constructs for use in S. cerevisiae (Wirshing and Goode, 2024). Thus, a similar strategy of using tandem copies of bright and photostable red fluorescent proteins can be explored for use in combination with mNG-Tpm in the future studies.
__ Complementation of tpm1∆ by Tpm2:__
I am confused about the quantification of Tpm2 expression by RT-PCR shown in Fig S3F. This figure shows that tpm2 mRNA expression levels are identical in cells with an empty plasmid or with a tpm2-encoding plasmid. In both strains (which lack tpm1), as well as in the WT control, one tpm2 copy is in the genome, but only one strain has a second tpm2 copy expressed from a centromeric plasmid, yet the results of the RT-PCR are not significantly different. (If anything, the levels are lower in the tpm2 plasmid-containing strain.) The methods state that the primers were chosen in the gene, so likely do not distinguish the genomic from the plasmid allele. However, the text claims a 1-fold increase in expression, and functional experiments show a near-complete rescue of the tpm1∆ phenotype. This is surprising and confusing and should be resolved to understand whether higher levels of Tpm2 are really the cause of the observed phenotypic rescue.
The authors could for instance probe for protein levels. I believe they have specific nanobodies against tropomyosin. If not, they could use expression of functional mNG-amTpm2 to rescue tpm1∆. Here, the expression of the protein can be directly visualized.
Response: __We thank the reviewer for pointing this out. We would like to clarify that in our RT-qPCR experiments, the primers were chosen within the Tpm1 and Tpm2 gene and do not distinguish between transcripts from endogenous or plasmid copy. We have now mentioned this in the Materials and Methods section of the revised manuscript. So, they represent a relative estimate of the total mRNA of these genes present in cells. We were consistently able to detect ~19 fold increase in Tpm2 total mRNA levels as compared to wildtype and ∆tpm1 cells (Fig. S4D) when tpm2 was expressed from a high-copy plasmid (pRS425). This increase in Tpm2 mRNA levels was accompanied by a rescue in growth (Fig. S4A) and actin cable organization (Fig. S4B) of ∆tpm1 cells containing pRS425-ptpm2TPM2. When tpm2 was expressed from a low-copy number centromeric plasmid (pRS316), we detected a ~2 fold increase in Tpm2 transcript levels when using the tpm1 promoter and no significant change was detected when using tpm2 promoter (Fig. S4E)__. We have made sure that these results are accurately described in the revised manuscript.
As per the reviewer's suggestion, we have now conducted a more extensive analysis to ascertain the expression levels of Tpm2 in our experiments and the data is now presented in new Figure S5. We used mNG-ASTpm1 and mNG-ASTpm2 to rescue growth of ∆tpm1 (Fig. S5A) and correlated growth rescue with protein levels using quantified fluorescence intensity (Fig. S5B, S5C) and western blotting (anti-mNG) (Fig. S5D, S5E). We find that ∆tpm1 cells containing pRS425-ptpm1mNG-ASTpm1 had the highest protein level followed by pRS425-ptpm2 mNG-ASTpm2, pRS305-ptpm1mNG-ASTpm1, and the least protein levels were found in pRS305-ptpm2 mNG-ASTpm2 containing ∆tpm1 cells in both fluorescence intensity and western blotting quantifications (Fig. S5C, S5E). Surprisingly, we were not able to detect any protein levels in ∆tpm1 cells containing pRS305-ptpm2 mNG-ASTpm2 with western blotting (Fig. S5D) which was also accompanied by a lack of growth rescue (Fig. S5A). This most likely due to weak expression from the native Tpm2 promoter which is consistent with previous literature (Drees et al., 1995). Taken together, this data clearly shows that the rescue observed in ∆tpm1 cells is caused due to increased expression of mNG-ASTpm2 in cells and supports our conclusion that increase in Tpm2 expression leads to restoration of normal growth and actin cables in ∆tpm1 cells.
__ Specific function of Tpm2:__
The data about the retrograde actin flow is interpreted as a specific function of Tpm2, but there is no evidence that Tpm1 does not also share this function. To reach this conclusion one would have to investigate retrograde actin flow in tpm1∆ (difficult as cables are weak) or for instance test whether Tpm1 expression restores normal retrograde flow to tpm2∆ cells.
Response: __We agree with the reviewer and as per the reviewer's suggestion, we have performed another experiment which include wildtype, ∆tpm2 cells containing empty pRS316 vector or pRS316-ptpm2TPM1 or pRS316-ptpm1TPM1. We find that RACF rate increased in ∆tpm2 cells as compared to wildtype and was restored to wildtype levels by exogenous expression of Tpm2 but not Tpm1 (Fig. S6E, S6F). Since, actin cables were not detectable in ∆tpm1 cells, we measured RACF rates in ∆tpm1 cells expressing Tpm1 or Tpm2 from a plasmid copy, which restored actin cables as shown previously in __Fig. 5A-C. We observed that RACF rates were similar to wildtype in ∆tpm1 cells expressing either Tpm1 or Tpm2 (Fig. S6E, S6F), suggesting that Tpm1 is not involved in RACF regulation. Taken together, these results suggest a specific role for Tpm2, but not Tpm1, in RACF regulation in S. cerevisiae, consistent with previous literature (Huckaba et al., 2006).
Minor comments: __1.__The growth of tpm1∆ with empty plasmid in Fig S3A is strangely strong (different from other figures).
Response: We thank the reviewer for pointing this out. We have now repeated the drop test multiple times (Fig. R2), but we see similar growth rates as the drop test already presented in Fig. S4A. __At this point, it would be difficult to ascertain the basis of this difference observed at 23{degree sign}C and 30{degree sign}C, but a recent study that links leucine levels to actin cable stability (Sing et al., 2022) might explain the faster growth of these ∆tpm1 cells containing a leu2 gene carrying high-copy plasmid. However, there is no effect on growth rate at 37{degree sign}C which is consistent with other spot assays shown in __Fig. S1D, S4F, S5A.
Significance
I am a cell biologist with expertise in both yeast and actin cytoskeleton.
The question of how tropomyosin localizes to specific actin networks is still open and a current avenue of study. Studies in other organisms have shown that different tropomyosin isoforms, or their acetylated vs non-acetylated versions, localize to distinct actin structures. Proposed mechanisms include competition with other ABPs and preference imposed by the formin nucleator. The current study re-examines the function and localization of the two tropomyosin proteins from the budding yeast and reaches the conclusion that they co-decorate all formin-assembled structures and also share most functions, leading to the simple conclusion that the more important contribution of Tpm1 is simply linked to its higher expression. Once consolidated, the study will appeal to researchers working on the actin cytoskeleton.
We thank the reviewer for their positive assessment of our work and the constructive feedback that has greatly improved the quality of our study. After addressing the points raised by the reviewer, we believe that our study has significantly gained in consolidating the major conclusions of our work.
**Referees cross-commenting**
Having read the other reviewers' comments, I do agree with reviewer 1 that it is not clear whether the Ala-Ser linker really mimics acetylation. I am less convinced than reviewer 3 that the key conclusions of the study are well supported, notably the issue of Tpm2 expression levels is not convincing to me.
Response: __We acknowledge the reviewer's point about the effect of Ala-Ser dipeptide and would request the reviewer to refer to our response to Reviewer 1 (Question 1) for a more detailed discussion on this. We have also extensively addressed the question of Tpm2 expression levels as suggested by the reviewer (new data in __Figure S5) which has further strengthened the conclusions of our study.
__Reviewer #3 (Evidence, reproducibility and clarity (Required)):
Summary:__ The study presents the first fully functional fluorescently tagged Tpm proteins, enabling detailed probing of Tpm isoform localization and functions in live cells. The authors created a modified fusion protein, mNG-amTpm, which mimicked native N-terminal acetylation and restored both normal growth and full-length actin cables in yeast cells lacking native Tpm proteins, demonstrating the constructs' full functionality. They also show that Tpm1 and Tpm2 do not have a preference for actin cables nucleated by different formins (Bnr1 and Bni1). Contrary to previous reports, the study found that overexpressing Tpm2 in Δtpm1 cells could restore growth rates and actin cable formation. Furthermore, it is shown that despite its evolutionary divergence, Tpm2 retains actin-protective functions and can compensate for the loss of Tpm1, contributing to cellular robustness.
Major and Minor Comments: 1. The key conclusions of this paper are convincing. However, I suggest that more detail be provided regarding the image analysis used in this study. Specifically, since threshold settings can impact the quality of the generated data and, therefore, its interpretation, it would be useful to see a representative example of the quantification methods used for actin cable length/number (as in refs. 80 and 81) and mitochondria morphology. These could be presented as Supplemental Figures. Additionally, it would help to interpret the results if the authors could be more specific about the statistical tests that were used.
Response: __We agree with the reviewer's suggestions and have now updated our Materials and Methods section to describe the image analysis pipelines used in more detail. We have also added examples of quantification procedure for actin cable length/number and mitochondrial morphology as an additional Supplementary __Figure S7. Briefly, the following pipelines were used:
- Actin cable length and number analysis: This was done exactly as mentioned in McInally et al., 2021, McInally et al., 2022. Actin cables were manually traced in Fiji as shown in __ S7A__, and then the traces files for each cell were run through a Python script (adapted from McInally et al., 2022) that outputs mean actin cable length and number per cell.
- Mitochondria morphology: Mitochondria Analyzer plug-in in Fiji was used to segment out the mitochondrial fragments. The parameters used for 2D segmentation of mitochondria were first optimized using "2D Threshold Optimize" to find the most accurate segmentation and then the same parameters were run on all images. After segmentation of the mitochondrial network, measurements of fragment number were done using "Analyze Particles" function in Fiji. An example of the overall process is shown in __ S7B.__ As per the reviewer's suggestion, we have now included the description of the statistical test used in the Figure Legends of each Figure in the revised manuscript. We have used One-Way Anova with Tukey's Multiple Comparison test, Kruskal-Wallis test with Dunn's Multiple Comparisons, and Unpaired Two-tailed t-test using the in-built functions in GraphPad Prism (v.6.04).
**Referees cross-commenting**
I agree with both reviewers 1 and 2 regarding the issues with the Ala-Ser acetylation mimic and Tpm2 expression levels, respectively. I think the authors should be more careful in how they frame the results, but I consider that these issues do not invalidate the main conclusions of this study.
Response: __We acknowledge the reviewer's concern about the Ala-Ser dipeptide and would request them to refer our earlier discussion on this in response to Reviewer 1 (Question 1) and Reviewer 2 (Question 2). We would also request the reviewer to refer to our answer to Reviewer 2 (Question 6) where we have extensively addressed the question of Tpm2 expression levels and their effect on rescue of Dtpm1 cells. This data is now presented as new __Figure S5 in our revised manuscript.
Reviewer#3 (Significance (Required)):
The finding that Tpm2 can compensate for the loss of Tpm1, restoring actin cable organization and normal growth rates, challenges previous assumptions about the non-redundant functions of these isoforms in Saccharomyces cerevisiae (ref. 16). It also supports a concentration-dependent and formin-independent localization of Tpm isoforms to actin cables in this species. The development of fully functional fluorescently tagged Tpm proteins is a significant methodological advancement. This advancement overcomes previous visualization challenges and allows for accurate in vivo studies of Tpm function and regulation in S. cerevisiae.
The findings will be of particular interest to researchers in the field of cellular and molecular biology who study actin cytoskeleton dynamics. Additionally, it will be relevant for those utilizing advanced microscopy and live-cell imaging techniques.
As a researcher, my experience lies in cytoskeleton dynamics and protein interactions, though I do not have specific experience related to tropomyosin. I use different yeast species as models and routinely employ live-cell imaging as a tool.
We thank the reviewer for their positive outlook and assessment of our study. We have incorporated all their suggestions, and we are confident that the revised manuscript has significantly improved in quality due to these additions.
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Referee #1
Evidence, reproducibility and clarity
There are 2 Major issues:
- Having an -ala-ser- linker between the GFP and tropomyosin mimics acetylation. This is not the case, and more likely the this linker acts as a spacer that allows tropomyosin polymers to form on the actin, and without it there is steric hindrance. A similar result would be seen with a simple flexible uncharged linker. It has been shown in a number of labs that the GFP itself masks the effect of the charge on the amino terminal methionine. This is consistent with NMR, crystallographic and cryo structural studies. Biochemical studies should be presented to demonstrate that the impact of a linker for the conclusions stated to be made, which provide the basis of a major part of this study.
- My major issue however is making the conclusions stated here, using an amino-terminal fluorescent protein tag that s likely to impact any type of isoform selection at the end of the actin polymer. Carboxyl terminal tagging may have a reduced effect, but modifying the ends of the tropomyosin, which are integral in stabilising end to end interactions with itself on the actin filament, never mind any section systems that may/maynot be present in the cell, is not appropriate.
Significance
This paper explores the role of formin in determining the localisation of different tropomyosins to different actin polymers and cellular locations within budding yeast. Previous studies have indicated a role for the actin nucleating proteins in recruiting different forms of tropomyosin within fission yeast. In mammalian cells there is variation in the role of formins in affiecting tropomyosin localisation - variation between cell type. There is also evidence that other actin binding proteins, and tropomyosin abundance play roles in regulating the tropomyosin-actin association according to cell type. Biochemical studies have previously been undertaken using budding yeast and fission yeast that the core actin polymerisation domain of formins do not interact with tropomyosin directly.
The significance of this study, given the above, and the concerns raised is not clear to this reviewer.
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www.biorxiv.org www.biorxiv.org
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Author response:
The following is the authors’ response to the original reviews
Public Reviews:
Reviewer #1 (Public review):
Summary:
Govindan and Conrad use a genome-wide CRISPR screen to identify genes regulating retention of intron 4 in OGT, leveraging an intron retention reporter system previously described (PMID: 35895270). Their OGT intron 4 reporter reliably responds to O-GlcNAc levels, mirroring the endogenous splicing event. Through a genome-wide CRISPR knockout library, they uncover a range of splicing-related genes, including multiple core spliceosome components, acting as negative regulators of OGT intron 4 retention. They choose to follow up on SFSWAP, a largely understudied splicing regulator shown to undergo rapid phosphorylation in response to O-GlcNAc level changes (PMID: 32329777). RNA-sequencing reveals that SFSWAP depletion not only promotes OGT intron 4 splicing but also broadly induces exon inclusion and intron splicing, affecting decoy exon usage. While this study offers interesting insights into intron retention and O-GlcNAc signaling regulation, the RNA sequencing experiments lack the essential controls needed to provide full confidence to the authors' conclusions.
Strengths:
(1) This study presents an elegant genetic screening approach to identify regulators of intron retention, uncovering core spliceosome genes as unexpected positive regulators of intron retention.
(2) The work proposes a novel functional role for SFSWAP in splicing regulation, suggesting that it acts as a negative regulator of splicing and cassette exon inclusion, which contrasts with expected SR-related protein functions.
(3) The authors suggest an intriguing model where SFSWAP, along with other spliceosome proteins, promotes intron retention by associating with decoy exons.
We thank the reviewer for recognizing and detailing the strengths of our manuscript.
Weaknesses:
(1) The conclusions on SFSWAP impact on alternative splicing are based on cells treated with two pooled siRNAs for five days. This extended incubation time without independent siRNA treatments raises concerns about off-target effects and indirect effects from secondary gene expression changes, potentially limiting confidence in direct SFSWAP-dependent splicing regulation. Rescue experiments and shorter siRNA-treatment incubation times could address these issues.
We repeated our SFSWAP knockdown analysis and analyzed both OGT e4-e5 junction splicing and SFSWAP transcript levels by RT-qPCR (now included in Sup. Fig. S4) from day 2 to day 5 post siRNA treatment. We observed that the time point at which OGT intron 4 removal increases (day 2) coincides with the time at which SFSWAP transcript levels start decrease, consistent with a direct effect of SFSWAP knockdown on OGT intron 4 splicing. Moreover, the effect of SFSWAP knockdown on OGT intron 4 splicing peaks between day 4-5, supporting our use of these longer time points to cast a wide net for SFSWAP targets.
(2) The mechanistic role of SFSWAP in splicing would benefit from further exploration. Key questions remain, such as whether SFSWAP directly binds RNA, specifically the introns and exons (including the decoy exons) it appears to regulate. Furthermore, given that SFSWAP phosphorylation is influenced by changes in O-GlcNAc signaling, it would be interesting to investigate this relationship further. While generating specific phosphomutants may not yield definitive insights due to redundancy and also beyond the scope of the study, the authors could examine whether distinct SFSWAP domains, such as the SR and SURP domains, which likely overlap with phosphorylation sites, are necessary for regulating OGT intron 4 splicing.
We absolutely agree with the reviewer that the current work stops short of a detailed mechanistic study, and we have made every attempt to be circumspect in our interpretations to reflect that limitation. In addition, we are very interested in delving more deeply into the mechanistic aspects of this regulation. In fact, we have initiated many of the experiments suggested by the reviewer (and more), but in each case, rigorous interpretable results will require a minimum another year’s time.
For example, we have used crosslinking and biotin labeling techniques (using previously available reagents from Eclipsebio) to test whether SFSWAP binds RNA. The results were negative, but the lack of strong SFSWAP antibodies required that we use a transiently expressed myc-tagged SFSWAP. Therefore, this negative result could be an artifact of the exogenous expression and/or tagging. Given the difficulties of “proving the negative”, considerably more work will be required to substantiate this finding. As another example, we intend to develop a complementation assay as suggested. For an essential gene, the ideal complementation system employs a degron system, and we have spent months attempting to generate a homozygous AID-tagged SFSWAP. Unfortunately, we so far have only found heterozygotes. Of course, this could be because the tag interferes with function, the insert was not efficiently incorporated by homologous repair, or that we simply haven’t yet screened a sufficient number of clones. We’re confident that these technical issues that can be addressed, but they will take a significant amount of time to resolve. While we would ideally define a mechanism, we think that the data reported here outlining functions for SFSWAP in splicing represent a body of work sufficient for publication.
(3) Data presentation could be improved (specific suggestions are included in the recommendations section). Furthermore, Excel tables with gene expression and splicing analysis results should be provided as supplementary datasheets. Finally, a more detailed explanation of statistical analyses is necessary in certain sections.
We have addressed all specific suggestions as detailed in the recommendations below.
Reviewer #2 (Public review):
Summary:
The paper describes an effort to identify the factors responsible for intron retention and alternate exon splicing in a complex system known to be regulated by the O-GlcNAc cycling system. The CRISPR/Cas9 system was used to identify potential factors. The bioinformatic analysis is sophisticated and compelling. The conclusions are of general interest and advance the field significantly.
Strengths:
(1) Exhaustive analysis of potential splicing factors in an unbiased screen.
(2) Extensive genome wide bioinformatic analysis.
(3) Thoughtful discussion and literature survey.
We thank the reviewer for recognizing and detailing the strengths of our manuscript.
Weaknesses:
(1) No firm evidence linking SFSWAP to an O-GlcNAc specific mechanism.
We couldn’t agree more with this critique. Indeed, our intention at the outset for the screen was to find an O-GlcNAc sensor linking OGT splicing with O-GlcNAc levels. As often occurs with high-throughput screens, we didn’t find exactly what we were looking for, but the screen nonetheless pointed us to interesting biology. Prompted by our screen, we describe new insights into the function of SFSWAP a relatively uncharacterized essential gene. Currently, we are testing other candidates from our screen, and we are performing additional studies to identify potential O-GlcNAc sensors.
(2) Resulting model leaves many unanswered questions.
We agree (see Reviewer 1, point 2 response).
Reviewer #3 (Public review):
Summary:
The major novel finding in this study is that SFSWAP, a splicing factor containing an RS domain but no canonical RNA binding domain, functions as a negative regulator of splicing. More specifically, it promotes retention of specific introns in a wide variety of transcripts including transcripts from the OGT gene previously studied by the Conrad lab. The balance between OGT intron retention and OGT complete splicing is an important regulator of O-GlcNAc expression levels in cells.
Strengths:
An elegant CRISPR knockout screen employed a GFP reporter, in which GFP is efficiently expressed only when the OGT retained intron is removed (so that the transcript will be exported from the nucleus to allow for translation of GFP). Factors whose CRISPR knockdown causes decreased intron retention therefore increase GFP, and can be identified by sequencing RNA of GFP-sorted cells. SFSWAP was thus convincingly identified as a negative regulator of OGT retained intron splicing. More focused studies of OGT intron retention indicate that it may function by regulating a decoy exon previously identified in the intron, and that this may extend to other transcripts with decoy exons.
We thank the reviewer for recognizing the strengths of our manuscript.
Weaknesses:
The mechanism by which SFSWAP represses retained introns is unclear, although some data suggests it can operate (in OGT) at the level of a recently reported decoy exon within that intron.
Interesting/appropriate speculation about possible mechanisms are provided and will likely be the subject of future studies.
We completely agree that this is a limitation of the current study (see above). Now that we have a better understanding of SFSWAP functions, we will continue to explore SFSWAP mechanisms as suggested.
Overall the study is well done and carefully described but some figures and some experiments should be described in more detail.
Recommendations for the authors:
Reviewer #1 (Recommendations for the authors):
(1) Clarify and add missing statistical details across the figures. For example, Figure S2 lacks statistical comparisons, and in Figures 4A and 4C the tests applied should be specified in the legend.
We have added appropriate statistical analysis wherever missing and edited figure legends to specify the tests used.
(2) The authors are strongly encouraged to provide detailed tables of gene expression and alternative splicing analyses from RNA-Seq experiments (e.g., edgeR, rMATS, Whippet, and MAJIQ), as this would enhance transparency and facilitate data interpretation.
We have added tables for gene expression and alternate splicing analysis as suggested (Suppl. tables 3-
6).
(3) Although the legend sometimes indicates differently (e.g., Figure 3b, 5a, 5c, etc), the volcano plots showing the splicing changes do not contain a cutoff for marginally differential percent spliced in or intron retention values.
The legends have been edited to reflect the correct statistical and/or PSI cutoffs.
(4) For consistency, use a consistent volcano plot format across all relevant figures (Figures 3b, 5a-c, S3, S4, S7, and S8), including cutoffs for differential splicing and the total count of up- and down-regulated events.
Due to different statistical frameworks and calculations employed by different alternate splicing pipelines, we could not use the same cutoffs for different pipelines. However, we have now indicated the number of up- and down-regulated events for consistency among the volcano plots.
(5) What is the overlap of differentially regulated events between the different analytical methodologies applied?
We analyzed the degree of overlap between the three pipelines used in the paper using a Venn diagram (added to Suppl. Fig. S7). However, as widely reported in literature (e.g., Olofsson et al., 2023; Biochem Biophys Res Commun. 2023; doi: 10.1016/j.bbrc.2023.02.053.), the degree of overlap between pipelines is quite low.
(6) To further substantiate your conclusions, additional validations of RNA-Seq splicing data, ideally visualized on an agarose gel, would be valuable, especially for exons and introns regulated by SFSWAP, and particularly for OGT decoy exons in Figure 4c.
We have not included these experiments as we focused on other critiques for this resubmission. Because the RNA-seq, RT-PCR and RT-qPCR data all align, we are confident that the products we are seeing are correctly identified and orthogonally validated (Figs 2d, 4a, 4b, and 4c).
(7) It would be more informative if the CRISPR screen data were presented in a format where both the adjusted p-value and LFC values of the hits are presented. Perhaps a volcano plot?
We have now included these graphs in revised Supplementary Figure S2.
(8) In Figure 2d, a cartoon showing primer binding sites for each panel could aid interpretation, particularly in explaining the unexpected simultaneous increase in OGT mRNA and intron retention upon SFSWAP knockdown.
We have added a cartoon showing primer binding sites similar to that shown in Fig. 4a.
(9) Page 9, line 1, states that SFSWAP autoregulates its expression by controlling intron retention. Including a Sashimi plot would provide visual support for this claim.
The data suggesting that SFSWAP autoregulates its own transcript abundance were reported in Zachar et al. (1994), not from our own studies. Validation of those data with our RNA-seq data is confounded by the fact that we are using siRNAs to knockdown the SFSWAP RNA at the transcript level (Fig. S15).
(10) In the legend of Figure S2 the authors state that negative results are inconclusive because RNA knockdowns are not verified by western blotting or qRT-PCR. This is correct, but the reviewer would also argue that the positive results are also inconclusive as they are not supported by a rescue experiment to confirm that the effect is not due to off-target effects.
This is a fair point with respect to the siRNA experiments on their own. However, the CRISPR screen was performed with sgRNAs, and MAGeCK RRA scores are high only for those genes that have multiple sgRNAs that up-regulate the gene. Examination of the SFSWAP sgRNAs individually shows that three of four SFSWAP sgRNAs had false discovery rates ≤10<sup>-42</sup> for GFP upregulation. Thus, the siRNAs provide an additional orthogonal approach. It seems unlikely that the siRNAs, and three independent sgRNAs will have the same off-target results. Thus, these combined observations support the conclusion that SFSWAP loss leads to decreased OGT intron retention.
(11) For clarity in Figure 3a, consider using differential % spliced in or intron retention bar plots with directionality (positive and negative axis) and labeling siSFSWAP as the primary condition.
(12) Consider presenting Figure 5D as a box plot with a Wilcoxon test for statistical comparison.
For both points 11 and 12, we have tried the graphs as the reviewer suggested. While these were good suggestions, in both cases we felt that the original plots ended up presenting a clearer presentation of the data (see Author response image 1).
Author response image 1.
(13) Please expand the Methods section to detail the Whippet and MAJIQ analyses.
We have expanded the methods section to include additional details of the alternate splicing analysis.
(14) Include coordinates for the four possible OGT decoy exon combinations analyzed in the Methods section.
We have added the coordinates of all four decoy forms in the methods section.
(15) A section on SFSWAP mass spectrometry is listed in Methods but is missing from the manuscript.
This section has now been removed.
Reviewer #2 (Recommendations for the authors):
This is an excellent contribution. The paper describes an effort to identify the factors responsible for intron retention and alternate exon splicing in a complex system known to be regulated by the O-GlcNAc cycling system. The CRISPR/Cas9 system was used to identify potential factors. The bioinformatic analysis is sophisticated and compelling. The conclusions are of general interest and advance the field significantly.
Some specific recommendations.
(1) The plots in Figure 3 describing SI and ES events are confusing to this reader. Perhaps the violin plot is not the best way to visualize these events. The same holds true for the histograms in the lower panel of Figure 3. Not sure what to make of these plots.
For Figure 3b, we include both scatter and violin plots to represent the same data in two distinct ways. For Figure 3d, we agree that these are not the simplest plots to understand, and we have spent significant time trying to come up with a better way of displaying these trends in GC content as they relate to SE and RI events. Unfortunately, we were unable to identify a clearer way to present these data.
(2) The model (Figure 6) is very useful but confusing. The legend and the Figure itself are somewhat inconsistent. The bottom line of the figure is apparent but I fear that the authors are trying to convey a more complete model than is apparent from this figure. Please revise.
We have simplified the figure from the previous submission. As mentioned above, we admit that mechanistic details remain unknown. However, we have tried to generate a model that reflects our data, adds some speculative elements to be tested in the future, but remains as simple as possible. We are not quite sure what the reviewer was referring to as “somewhat inconsistent”, but we have attempted to clarify the model in the revised Discussion and Figure legend.
(3) It is unclear how normalization of the RNA seq experiments was performed (eg. Figure S5 and 6).
The normalization differences in Fig. S5 and S6 (now Fig S8 and S9) were due to scaling differences during the use of rmats2sashimiplot software. We have now replaced Fig. S5 to reflect correctly scaled images.
I am enthusiastic about the manuscript and feel that with some clarification it will be an important contribution.
Thank you for these positive comments about our study!
Reviewer #3 (Recommendations for the authors):
(1) In Figure 1f, it is clear that siRNA-mediated knockdown of OGT greatly increases spliced RNA as the cells attempt to compensate by more efficient intron removal (three left lanes). However, there is no discussion of the various treatments with TG or OSMI. Might quantitation of these lanes not also show the desired effects of TG and OSMI on spliced transcript levels?
The strong effect of OGT knockdown masks the (comparatively modest) effects of subsequent inhibitor treatments on the reporter RNA. We have edited the results section to clarify this.
(2) In Figure 2c, why is the size difference between spliced RNA and intron-retained RNA so different in the GFP-probed gel (right) compared with the OGT-probed gel (left)? Even recognizing that the GFP probe is directed against reporter transcripts, and the OGT probe (I think) is directed against endogenous OGT transcripts, shouldn't the difference between spliced and unspliced bands be the same, i.e., +/- the intron 4 sequence. Also, why does the GFP probe detect the unspliced transcript so poorly?
The fully spliced endogenous OGT mRNA is ~5.5 kb while the fully spliced reporter is only ~1.6kb, so the difference in size (the apparent shift relative to the mRNA) is quite different. Moreover, the two panels in Fig 2c are not precisely scaled to one another, so direct comparisons cannot be made.
The intron retained isoform does not accumulate to high levels in this reporter, a phenotype that we also observed with our GFP reporter designed to probe the regulation of the MAT2A retained intron (Scarborough et al., 2021). We are not certain about the reason for these observations, but suspect that the reporter RNA’s retained intron isoforms are less stable in the nucleus than their endogenous counterparts. Alternatively, the lack of splicing may affect 3´ processing of the transcripts so that they do not accumulate to the high levels observed for the wild-type genes.
(3) Please provide more information about the RNA-seq experiments. How many replicates were performed under each of the various conditions? The methods section says three replicates were performed for the UPF1/TG experiments; was this also true for the SFSWAP experiments?
All RNA-seq experiments were performed in biological triplicates. We have edited the methods section to clarify this.
(4) Relatedly, the several IGV screenshots shown in Figure 3C presumably represent the triplicate RNA seq experiments. In part D, how many experiments does the data represent? Is it a compilation of three experiments?
Fig. 3d is derived from alternate splicing analysis performed on three biological replicates. We have added the number of replicates (n=3) on the figure to clarify this. We have also noted that the three IGV tracks represent biological replicates in the Figure legend for 3c.
(5) Please provide more details regarding the qRT-PCR experiments.
We have provided the positions of primer sets used for RT-qPCR analysis and cartoon depictions of target sites below the data wherever appropriate.
(6) In the discussion of decoy exon function (in the Discussion section), several relevant observations are cited to support a model in which decoy exons promote assembly of splicing factors. One might also cite the finding that eCLIP profiling has found enriched binding of U2AF1 and U2AF2 at the 5' splice site region of decoy exons (reference 16).
Excellent point. This has now been added to the Discussion.
Minor corrections / clarifications:
(1) In the Figure 2A legend, CRISPR is misspelled.
Corrected.
(2) In the discussion, the phrase "indirectly inhibits splicing of exons 4 and 5, but promoting stable unproductive assembly of the spliceosome", the word "but" should probably be "by".
Corrected.
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Reviewer #2 (Public review):
Summary
In this paper, the function of trpγ in lipid metabolism was investigated. The authors found that lipid accumulation levels were increased in trpγ mutants and remained high during starvation; the increased TAG levels in trpγ mutants were restored by the expression of active AMPK in DH44 neurons and oral administration of the anti-diabetic drug metformin. Furthermore, oral administration of lipase, TAG and free fatty acids effectively restored survival of trpγ mutants under starvation conditions. These results indicate that TRPv plays an important role in the maintenance of systemic lipid levels through the proper expression of lipase. Furthermore, authors have shown that this function is mediated by DH44R2. This study provides an interesting finding in that the neuropeptide DH44 released from the brain regulates lipid metabolism through a brain-gut axis, acting on the receptor DH44R2 expressed in gut cells.
Strengths
Using Drosophila genetics, careful analysis of which cells express trpγ regulates lipid metabolism is performed in this study. The study supports its conclusions from various angles, including not only TAG levels, but also fat droplet staining and survival rate under starved conditions, and oral administration of substances involved in lipid metabolism.
Weaknesses
The function of lipases, as well as identification of cell types, in the DH44R2-expressing cells in the gut can be investigated.
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Reviewer #3 (Public review):
In this manuscript, the authors demonstrated the significance of the TRPγ channel in regulating internal TAG levels. They found high TAG levels in TRPγ mutant, which was ascribed to a deficit in the lipolysis process due to the downregulation of brummer (bmm). It was notable that the expression of TRPγ in DH44+ PI neurons, but not dILP2+ neurons, in the brain restored the internal TAG levels and that the knockdown of TRPγ in DH44+ PI neurons resulted in an increase in TAG levels. These results suggested a non-cell autonomous effect of Dh44+PI neurons. Additionally, the expression of the TRPγ channel in Dh44 R2-expressing cells restored the internal TAG levels. The authors, however, did not provide an explanation of how TRPγ might function in both presynaptic and postsynaptic cells in the non-cell autonomous manner to regulate the TAG storage. The authors further determined the effect of TRPγ mutation on the size of lipid droplets (LD) and the lifespan and found that TRPγ mutation caused an increase in the size of LD and a decrease in the lifespan, which were reverted by feeding lipase and metformin. These were creative endeavors, I thought. The finding that DH44+ PI neurons have non-cell autonomous functions in regulating bodily metabolism (mainly sugar/lipid) in addition to directing sugar nutrient sensing and consumption is likely correct, but the paper has many loose ends.
Comments on revisions:
The authors have addressed nearly all of my concerns with additional experiments and explanations.
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Author response:
The following is the authors’ response to the original reviews
Public Reviews:
Reviewer #1 (Public Review):
Summary:
This research article by Nath et al. from the Lee Lab addresses how lipolysis under starvation is achieved by a transient receptor potential channel, TRPγ, in the neuroendocrine neurons to help animals survive prolonged starvation. Through a series of genetic analyses, the authors identify that TRPγ mutations specifically lead to a failure in lipolytic processes under starvation, thereby reducing animals' starvation resistance. The conclusion was confirmed through total triacylglycerol levels in the animals and lipid droplet staining in the fat bodies. This study highlights the importance of transient receptor potential (TRP) channels in the fly brain to modulate energy homeostasis and combat metabolic stress. While the data is compelling and the message is easy to follow, several aspects require further clarification to improve the interpretation of the research and its visibility in the field.
Strengths:
This study identifies the biological meaning of TRPγ in promoting lipolysis during starvation, advancing our knowledge about TRP channels and the neural mechanisms to combat metabolic stress. Furthermore, this study demonstrates the potential of the TRP channel as a target to develop new therapeutic strategies for human metabolic disorders by showing that metformin and AMPK pathways are involved in its function in lipid metabolisms during starvation in Drosophila.
Weaknesses:
Some key results that might strengthen their conclusions were left out for discussion or careful explanation (see below). If the authors could improve the writing to address their findings and connect their findings with conclusions, the research would be much more appreciated and have a higher impact in the field.
Here, I listed the major issues and suggestions for the authors to improve their manuscript:
(1) Are the increased lipid droplet size and the upregulated total TAG level measured in the starved or sated mutant in Figure 1? This information might be crucial for readers to understand the physiological function of TRP in lipid metabolism. In other words, clarifying whether the upregulated lipid storage is observed only in the starved trp mutant will advance our knowledge of TRPγ. If the increase of total TAG level is only observed in the starved animals, TRP in the Dh44 neurons might serve as a sensor for the starvation state required to promote lipolysis in starvation conditions. On the other hand, if the total TAG level increases in both starved and sated animals, activation of Dh44 through TRPγ might be involved in the lipid metabolism process after food ingestion.
We measured total TAG level in Figure 1 and LD sizes in Figure 2 under sated condition. We inserted “under sated condition” to clarify it. lines 97 and 147-148.
Thanks for your suggestions.
(2) It is unclear how AMPK activation in Dh44 neurons reduces the total triacylglycerol (TAG) levels in the animals (Figure 3G). As AMPK is activated in response to metabolic stress, the result in Figure 3G might suggest that Dh44 neurons sense metabolic stress through AMPK activation to promote lipolysis in other tissues. Do Dh44 neurons become more active during starvation? Is activation of Dh44 neurons sufficient to activate AMPK in the Dh44 neurons without starvation? Is activation of AMPK in the Dh44 neurons required for Dh44 release and lipolysis during starvation? These answers would provide more insights into the conclusion in Lines 192-193.
In our previous study, we demonstrated that trpγ mutants exhibited lower levels of glucose, trehalose and glycogen level (Dhakal et al. 2022), and in the current study, we observed excessive lipid storage in the trpγ mutant, indicating imbalanced energy homeostasis. Given the established role of AMPK in maintaining energy balance (Marzano et. al., 2021, Lin et al 2021), we employed the activated form of AMPK (UAS-AMPK<sup>TD</sup>) in our experiments. Our result showed that expression of activated AMPK in Dh44 neurons led to a reduction in total TAG levels, suggesting that AMPK activation in these neurons can promote lipolysis even in the absence of starvation. Regarding the activation of Dh44 neurons, Dus et al in 2015 reported that Dh44 cells in the brain are activated by nutritive sugars especially in starvation conditions. In addition, another report showed a role of Dh44 neuron in regulating starvation induced sleep suppression (Oh et. al., 2023) which may imply that these neurons become more active under starved conditions. We did not directly assess whether Dh44 neuron activity increases during starvation or whether AMPK activation in these neurons is required for DH44 release and subsequent lipolysis, our finding support the notion that AMPK activation in Dh44 neuron is sufficient to reduce TAG levels, potentially by metabolic stress response typically observed during starvation. We explained it like the following: “Dh44 neurons regulate starvation-induced sleep suppression (Oh et. al., 2023), which implies that these neurons become more active under starved conditions.” lines 190-191.
(3) It is unclear how the lipolytic gene brummer is further downregulated in the trpγ mutant during starvation while brummer is upregulated in the control group (Figure 6A). This result implies that the trpγ mutant was able to sense the starvation state but responded abnormally by inhibiting the lipolytic process rather than promoting lipolysis, which makes it more susceptible to starvation (Figure 3B).
Thanks for your suggestions. We explained it like the following: “The data indicates that the trpg mutant can sense the starvation state but responds abnormally by suppressing lipolysis instead of activating it. This dysregulated lipolytic response likely increases the mutant's vulnerability to starvation, as it cannot effectively mobilize lipid stores for energy during periods of nutrient deprivation.” lines 251-254.
(4) There is an inconsistency of total TAG levels and the lipid droplet size observed in the Dh44 mutant but not in the Dh44-R2 mutant (Figures 7A and 7F). This inconsistency raises a possibility that the signaling pathway from Dh44 release to its receptor Dh44-R2 only accounts for part of the lipid metabolic process under starvation. Adding discussion to address this inconsistency may be helpful for readers to appreciate the finding.
Thanks for your suggestion. We included the following in the Discussion: “There is an inconsistency of total TAG levels and the LD size observed in the Dh44 mutant. This inconsistency raises a possibility that the signaling pathway from DH44 release to its receptor DH44R2 only accounts for part of the lipid metabolic process under starvation. While Dh44 mutant flies displayed normal internal TAG levels, Dh44R2 mutant flies exhibited elevated TAG levels. This suggested that the lipolysis phenotype could be facilitated by a neuropeptide other than DH44. Alternatively, a DH44 neuropeptide-independent pathway could mediate the lipolysis.” lines 429-436.
Reviewer #2 (Public Review):
Summary:
In this paper, the function of trpγ in lipid metabolism was investigated. The authors found that lipid accumulation levels were increased in trpγ mutants and remained high during starvation; the increased TAG levels in trpγ mutants were restored by the expression of active AMPK in DH44 neurons and oral administration of the anti-diabetic drug metformin. Furthermore, oral administration of lipase, TAG, and free fatty acids effectively restored the survival of trpγ mutants under starvation conditions. These results indicate that TRPv plays an important role in the maintenance of systemic lipid levels through the proper expression of lipase. Furthermore, authors have shown that this function is mediated by DH44R2. This study provides an interesting finding in that the neuropeptide DH44 released from the brain regulates lipid metabolism through a brain-gut axis, acting on the receptor DH44R2 presumably expressed in gut cells.
Strengths:
Using Drosophila genetics, careful analysis of which cells express trpγ regulates lipid metabolism is performed in this study. The study supports its conclusions from various angles, including not only TAG levels, but also fat droplet staining and survival rate under starved conditions, and oral administration of substances involved in lipid metabolism.
Weaknesses:
Lipid metabolism in the gut of DH44R2-expressing cells should be investigated for a better understanding of the mechanism. Fat accumulation in the gut is not mechanistically linked with fat accumulation in the fat body. The function of lipase in the gut (esp. R2 region) should be addressed, e.g. by manipulating gut-lipases such as magro or Lip3 in the gut in the contest of trpγ mutant. Also, it is not clarified which cell types in the gut DH44R2 is expressed. The study also mentioned only in the text that bmm expression in the gut cannot restore lipid droplet enlargement in the fat body, but this result might be presented as a figure.
We appreciate the reviewer’s insightful suggestions. Unfortunately, due to the unviability of the reagent (UAS-Lip3), we were unable to manipulate gut lipase in trpy mutants as proposed. However, we additionally performed immunostaining to examine the co-expression of trpγ and Dh44R2 in the gut, and our results indicate that both trpγ and Dh44R2 are co-expressed in the R2 region of the gut (Figure 7O and P). Furthermore, we have updated our figures to address the point that bmm expression in the gut does not restore lipid droplet enlargement in the fat body, with the revised version (Figure 5I and J).
Reviewer #3 (Public Review):
In this manuscript, the authors demonstrated the significance of the TRPγ channel in regulating internal TAG levels. They found high TAG levels in TRPγ mutant, which was ascribed to a deficit in the lipolysis process due to the downregulation of brummer (bmm). It was notable that the expression of TRPγ in DH44+ PI neurons, but not dILP2+ neurons, in the brain restored the internal TAG levels and that the knockdown of TRPγ in DH44+ PI neurons resulted in an increase in TAG levels. These results suggested a non-cell autonomous effect of Dh44+PI neurons. Additionally, the expression of the TRPγ channel in Dh44 R2-expressing cells restored the internal TAG levels. The authors, however, did not provide an explanation of how TRPγ might function in both presynaptic and postsynaptic cells in the non-cell autonomous manner to regulate the TAG storage. The authors further determined the effect of TRPγ mutation on the size of lipid droplets (LD) and the lifespan and found that TRPγ mutation caused an increase in the size of LD and a decrease in the lifespan, which were reverted by feeding lipase and metformin. These were creative endeavors, I thought. The finding that DH44+ PI neurons have non-cell autonomous functions in regulating bodily metabolism (mainly sugar/lipid) in addition to directing sugar nutrient sensing and consumption is likely correct, but the paper has many loose ends. I would like to see a revision that includes more experiments to tighten up the findings and appropriate interpretations of the results.
(1) The authors need to provide interpretations or speculations as to how DH44+ PI neurons have non-cell autonomous functions in regulating the internal TAG stores, and how both presynaptic DH44 neurons and postsynaptic DH44 R2 neurons require TRPγ for lipid homeostasis.
In Discussion, we had mentioned our previous finding. “ We previously proposed that TRPg holds DH44 neurons in a state of afterdepolarization, thus reducing firing rates by inactivating voltage-gated Na+ channels (Dhakal et al., 2022). At the physiological level, this induces the consistent release of DH44 and depletion of DH44 stores, resulting in nutrient utilization and storage malfunctions.”
We also included the following: “TRPg in DH44 neurons may influence the release of metabolic signals or hormones that act on postsynaptic DH44R2 cells. These postsynaptic cells could, in turn, modulate lipid storage and metabolism in a non-cell autonomous manner. However, the mechanism by which TRPg functions in DH44R2 cells remains unclear. One possible explanation is that TRPg in the gut may be activated by stretch or osmolarity (Akitake et al. 2015).” lines 439-440.
This interaction between presynaptic and postsynaptic cells may ensure a coordinated response to metabolic changes and maintain lipid homeostasis. Thus, both Dh44-expressing and Dh44-R2-expressing cells are crucial for the proper functioning of TRPγ in regulating internal TAG levels and lipid storage.
(2) The expression of TRPγ solely in DH44 R2 neurons of TRPγ mutant flies restored the TAG phenotype, suggesting an important function mediated by TRPγ in DH44 R2 neurons. However, the authors did not document the endogenous expression of TRPγ in the DH44R2+ gut cells. This needs to be shown.
We appreciate the reviewer’s suggestion. To address this, we performed immunostaining to examine the expression of TRPγ in the DH44R2+ gut cells. Our results, as shown in Figure 7 O and P, confirm that TRPγ is co-expressed in the Dh44R2+ cells in the gut. We also found that Dh44R2 is expressed in the brain as well. We documented this part like the following: “Given that Dh44R2 is predominantly expressed in the intestine, we performed immunostaining to examine whether Dh44R2 co-localizes with trpg in gut cells. Our results confirmed that Dh44R2 and trpg are co-expressed in intestinal cells (Figure 7O and P). Additionally, we analyzed Dh44R2 expression in the brain and found that two Dh44R2-expressing cells are co-localized with Dh44-expressing cells in the PI region (Figure 7Q). To further delineate whether Dh44R2-mediated fat utilization is specific to the brain, gut, or fat body, we knocked down Dh44R2<sup>RNAi</sup> using Dh44-GAL4, myo1A-GAL4, and cg-GAL4, respectively (Figure 7–figure supplement 1E). Notably, knockdown of Dh44R2 with Myo1A-GAL4 resulted in elevated TAG levels, indicating that DH44R2 activity in lipid metabolism is specific to the gut.” lines 375-384.
(3) While Dh44 mutant flies displayed normal internal TAG levels, Dh44R2 mutant flies exhibited elevated TAG levels (Figure 7A). This suggested that the lipolysis phenotype could be facilitated by a neuropeptide other than Dh44. Alternatively, a Dh44 neuropeptide-independent pathway could mediate the lipolysis. In either case, an additional result is needed to substantiate either one of the hypotheses.
The Dh44 mutant flies exhibited normal TAG levels, whereas Dh44R2 mutant flies showed elevated TAG levels. However, when we examined the lipid droplets in the fat body, both Dh44 mutant and Dh44R2 mutant flies displayed larger lipid droplets, indicating a disruption in lipid metabolism. Additionally, we assessed starvation survival time and found that both Dh44 and Dh44R2 mutant flies exhibited reduced survival under starvation conditions compared to controls. Supplementation with lipase (Figure 7–figure supplement 1A), glycerol (Figure 7–figure supplement 1B), hexanoic acid (Figure 7–figure supplement 1C), and mixed TAGs (Figure 7–figure supplement 1D) improved starvation survival time, further supporting that the lipid metabolism pathway was impaired in both mutants. These observations highlight the role of Dh44 in regulating lipolysis. We included related Discussion: “There is an inconsistency of total TAG levels and the LD size observed in the Dh44 mutant. This inconsistency raises a possibility that the signaling pathway from DH44 release to its receptor DH44R2 only accounts for part of the lipid metabolic process under starvation. While Dh44 mutant flies displayed normal internal TAG levels, Dh44R2 mutant flies exhibited elevated TAG levels. This suggested that the lipolysis phenotype could be facilitated by a neuropeptide other than DH44. Alternatively, a DH44 neuropeptide-independent pathway could mediate the lipolysis.” lines 429-436.
(4) While the authors observed an increased area of fat body lipid droplets (LD) in Dh44 mutant flies (Figure 7F), they did not specify the particular region of the fat body chosen for measuring the LD area.
We have chosen the 2-3 segment in the abdomen for all fat body images, which we already mentioned in Nile red staining in the Method section line 630-631.
(5) The LD area only accounts for TAG levels in the fat body, whereas TAG can be found in many other body parts, including the R2 area as demonstrated in Figure 5A-D using Nile red staining. As such, measuring the total internal TAG levels would provide a more accurate representation of TAG levels than the average fat body LD area.
We have measured total internal TAG level in whole body throughout the experiments (Figure 1F, 2C, 2E, 3C, 3G, 4A, 4B, 7A, 7I, and many Supplementary Figures) except bmm expression using GAL4/UAS system. Now we include this new data in Figure 5–figure supplement 1) which is the same conclusion with LD analysis.
(6) In Figure 5F-I, the authors should perform the similar experiment with Dh44, Dh44R1, and Dh44R2 mutant flies.
We did the experiments with Dh44, Dh44R1, and Dh44R2 mutant flies and we found that Dh44 and Dh44R2 mutant flies showed reduced starvation survival time than control and which was increased after supplementation of lipase, glycerol, hexanoic acid and TAG (Figure 7– figure supplement 1A–D). lines 361-372.
(7) The representative image in Figure 6B does not correspond to the GFP quantification results shown in Figure 6C. In trpr1;bmm::GFP flies, the GFP signal appears stronger in starved conditions than in satiated conditions.
We updated it with new images. We quantified GFP intensity level using image J and found that GFP intensity level was significantly lower in starved condition in trpγ<sup>1</sup>;bmm::GFP flies than sated condition.
(8) In Figure 6H-I, fat body-specific expression of bmm reversed the increased LD area in TRPγ mutants. The authors also showed that Dh44+PI neuron-specific expression of bmm yielded a similar result. The authors need to provide an interpretation as to how bmm acts in the fat body or DH44 neurons to regulate this.
We first inserted the following in results: “Furthermore, the expression of bmm in the fat body, as well as Dh44 neurons in the PI region, can promote lipolysis at the systemic level.” lines 276-277.
Additionally, we discussed it in the Discussion: “Brummer lipase is essential for regulating lipid levels in the insect fat body by mediating lipid mobilization and energy homeostasis. In Nilaparvata lugens, it facilitates triglyceride breakdown (Lu et al., 2018), while studies in Drosophila show that reduced Brummer lipase expression decreases fatty acids and increases diacylglycerol levels, highlighting its role in lipid metabolism (Nazario-Yepiz et al., 2021). Here, we additionally demonstrate that bmm expression in DH44 neurons within the PI region can systemically regulate TAG levels. Cell signaling or energy status in DH44 neurons may contribute to hormonal release that targets organs such as the fat body.” lines 451-459.
(9) The authors should explain why the DH44 R1 mutant did not represent similar results as the wild type.
We added “In addition, bmm levels in Dh44R1<sup>Mi</sup> under starved condition did not increase as significantly as in the control. This suggests a unique role of DH44 and its receptors in regulating lipid metabolism and response to nutritional status in Drosophila.” lines 358-360.
(10) It would be good to have a schematic that represents the working model proposed in this manuscript.
We updated the schematic model in revised version (Figure 8).
Recommendations for the authors:
Reviewing Editor (Recommendations For The Authors):
This paper characterized the function of trpγ in Dh44-expressing PI neurons for lipid metabolism and lipolysis induced by prolonged starvation. The authors applied a series of lipolytic genetic manipulation and lipid/lipid metabolism supplements to rescue the trpγ deficits in lipolysis: the expression of active AMPK in the DH44-expressing PI neurons or brummer, a lipolytic gene, in the trpγ-expressing cells, and oral administration of the anti-diabetic drug metformin, lipase, TAG and free fatty acids. Despite this exhaustive characterization of the defective lipolysis in the trpγ mutants, there remain puzzles in inconsistent defects of Dh44 and DH44R2 in the total TAG levels and in the expression and functions of the receptor in the gut. Clarification of these points and other issues raised by the reviewers should improve the mechanisms of lipid metabolism through Dh44 signalling.
Reviewer #1 (Recommendations For The Authors):
(1) It might be worth introducing Dh44 in the introduction section as it is unclear to readers how the authors hypothesized the site-of-action of TRPγ in Dh44 neurons for lipid metabolism after reading the introduction.
We introduced the following: “We found that TRPg expression in Dh44 neuroendocrine cells in the brain is critical for maintaining normal carbohydrate levels in tissues (Dhakal et al. 2022). Building on this, we hypothesized that TRPg in Dh44 cells also regulates lipid and protein homeostasis.” lines 69-71.
(2) Providing a summary model in the end to integrate the present findings and their previous publication about TRPγ functions in Drosophila sugar selection would greatly help readers understand and appreciate the general role of TRPγ in balancing energy homeostasis.
We made a schematic model in Figure 8.
(3) Swapping the order of Figures 5 and 6 might be a better way to tell the story without logic gaps. The results addressing the mechanisms of metformin and TRPγ in promoting lipolysis under starvation are interrupted by the lipid storage data in the R2 cells in the current Figure 5A-5E. In addition, presenting Figure 5A-5E before or together with Figure 7 will help readers appreciate the expression of Dh44-R2 and its function in regulating lipid metabolism in Figure 7.
We did.
(4) It might be misleading to use the word "sated" for the condition of 5-hour mild starvation. The word "mild starvation" or the equivalents might be a better word choice.
We appreciate the reviewer’s concern. As hemolymph sugar level does not drop down significantly in 5 hr starvation, the previous papers (Dus et al 2015, Dhakal et al 2022) indicated it as sated condition. To use the word consistently, we prefer using “sated” instead of “mild starvation”.
(5) It is unclear what the white arrows are pointing at in Figures 7O and 7P. Some of those seem to be non-specific signals, so it is hard to connect the figure to the conclusion in Lines 351-353. It would be helpful to add some explanations to help readers interpret Figures 7O and 7P.
In the previous version, Figure 7O and 7P white arrows represented the expression of Dh44R2 in the SEZ region of the brain and R2 region of the gut. In revised version, to make clear, we performed additional immunostaining for the co-expression of trpγ and Dh44R2 in the gut. We found that trpγ and Dh44R2 co-expressed at the R2 region of the gut specifically (Figure 7O and P). Similarly, we found that two cells of Dh44R2 co-expressed in Dh44 cells in the PI region of the brain (now Figure 7Q). We updated this part. lines 375-380.
(6) The figure legend for the (G) panel in Figure 2-figure Supplement 1 was mislabeled as (F).
We corrected it.
(7) In Line 85, the authors might want to write "… among these mutants, only trpγ mutant displayed reduced carbohydrate levels, suggesting …". Please confirm the information for the sentence. lines 87-88.
We clarified it.
Reviewer #2 (Recommendations For The Authors):
(1) The trpγ[G4] would be difficult for non-Drosophila researchers to understand; it would be better to use trpγ-Gal4.
We got the mutant line from Dr. Craig Montell who named it. We explained it like the following in the main text: “controlled by GAL4 knocked into the trpg locus (trpg<sup>G4</sup> flies; +)” line 109.
(2) The arrows in Figures 7O and 7P need to be explained in the figure legends.
We did.
Reviewer #3 (Recommendations For The Authors):
(11) Lines 95-96 should have a reference.
We did.
(12) Lines 129-130: It should read "TRPγ expressed in DH44 cells is sufficient for the regulation of lipid levels."
We changed it as suggested.
(13) Figure 5E needs to be repeated with more trials.
We increased the n numbers. Previously (Figure 5E) we included area of 10 LDs from 3 samples, and in revised figure (Figure 6I) we have included 28 LDs from 10 samples.
(14) Figures 5F-I, bold lines are not too visible and therefore, dotted lines could be used.
We changed it as suggested.
(15) Line 356: It is not true that D-trehalose or D-fructose is commonly detected by DH44 neurons. These sugars at concentrations much higher than the physiological concentration range stimulate DH44 neurons (see Dus et al., 2015).
We removed it.
(16) Lines 362-363: It should read "Expression of TRPγ in DH44 neurons was necessary and sufficient to regulate the carbohydrate and lipid levels.".
We changed it.
(17) Lines 369-370: The authors need to consider removing the possible role of CRF in regulating lipid homeostasis. It could be considered to be far-fetched.
We removed it.
(18) Line 407-408: the sentence "Nevertheless, it is also known that DH44 neurons mediate the influence of dietary amino acids on promoting food intakes in flies (37)" needs to be removed. They used amino acid concentrations that were far greater than the physiological levels observed in the internal milieu of flies. Still, many laboratories cannot reproduce the result of using the high AA concentrations.
We removed it.
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Reviewer #1 (Public review):
Summary:
Inhibitory hM4Di and excitatory hM3Dq DREADDs are currently the most commonly utilized chemogenetic tools in the field of nonhuman primate research, but there is a lack of available information regarding the temporal aspects of virally-mediated DREADD expression and function. Nagai et al. investigated the longitudinal expression and efficacy of DREADDs to modulate neuronal activity in the macaque model. The authors demonstrate that both hM4Di and hM3Dq DREADDs reach peak expression levels after approximately 60 days and are stably expressed for a period of at least 1.5 years in the macaque brain. During this period, DREADDs effectively modulated neuronal activity, as evidenced by a variety of measures, including behavioural testing, functional imaging, and/or electrophysiological recording. Notably, some of the data suggest that DREADD expression may decline after two years. This is a novel finding and has important implications for the utilization of this technology for long-term studies, as well as its potential therapeutic applications. Lastly, the authors highlight that peak DREADD expression may be significantly influenced by the choice of viral titer and the expressed protein tag, emphasizing the importance of careful design and selection of viral constructs for neuroscientific research. This study represents a critical step in the field of chemogenetics, setting the scene for future development and optimization of this technology.
Strengths:
The longitudinal approach of this study provides important preliminary insights into the long-term utility of chemogenetics, which has not yet been thoroughly explored.
The data presented are novel and inclusive, relying on well-established in vivo imaging methods, as well as behavioral and immunohistochemical techniques. The conclusions made by the authors are generally supported by a combination of these techniques. In particular, the utilization of in vivo imaging as a non-invasive method is translationally relevant and likely to make an impact in the field of chemogenetics, such that other researchers may adopt this method of longitudinal assessment in their own experiments. Rigorous standards have been applied to the datasets, and the appropriate controls have been included where possible.
The number of macaque subjects (20) from which data was available is also notable. Behavioral testing was performed in 11 subjects, FDG-PET in 5, electrophysiology in 1, and [11C]DCZ-PET in 15. This is an impressive accumulation of work that will surely be appreciated by the growing community of researchers using chemogenetics in nonhuman primates.
The implication that chemogenetic effects can be maintained for up to 1.5-2 years, followed by a gradual decline beyond this period, is an important development in knowledge. The limited duration of DREADD expression may present an obstacle in the translation of chemogenetic technology as a potential therapeutic tool, and it will be of interest for researchers to explore whether this limitation can be overcome. This study therefore represents a key starting point upon which future research can build.
Weaknesses:
Overall, the conclusions of the paper are mostly supported by the data but may be overstated in some cases, and some details are also missing or not easily recognizable within the figures. The provision of additional information and analyses would be valuable to the reader and may even benefit the authors' interpretation of the data.
The conclusion that DREADD expression gradually decreases after 1.5-2 years is only based on a select few of the subjects assessed; in Figure 2, it appears that only 3 hM4Di cases and 2 hM3Dq cases are assessed after the 2-year timepoint. The observed decline appears consistent within the hM4Di cases, but not for the hM3Dq cases (see Figure 2C: the AAV2.1-hSyn-hM3Dq-IRES-AcGFP line is increasing after 2 years.)
Given that individual differences may affect expression levels, it would be helpful to see additional labels on the graphs (or in the legends) indicating which subject and which region are being represented for each line and/or data point in Figure 1C, 2B, 2C, 5A, and 5B. Alternatively, for Figures 5A and B, an accompanying table listing this information would be sufficient.
While the authors comment on several factors that may influence peak expression levels, including serotype, promoter, titer, tag, and DREADD type, they do not comment on the volume of injection. The range in volume used per region in this study is between 2 and 54 microliters, with larger volumes typically (but not always) being used for cortical regions like the OFC and dlPFC, and smaller volumes for subcortical regions like the amygdala and putamen. This may weaken the claim that there is no significant relationship between peak expression level and brain region, as volume may be considered a confounding variable. Additionally, because of the possibility that larger volumes of viral vectors may be more likely to induce an immune response, which the authors suggest as a potential influence on transgene expression, not including volume as a factor of interest seems to be an oversight.
The authors conclude that vectors encoding co-expressed protein tags (such as HA) led to reduced peak expression levels, relative to vectors with an IRES-GFP sequence or with no such element at all. While interesting, this finding does not necessarily seem relevant for the efficacy of long-term expression and function, given that the authors show in Figures 1 and 2 that peak expression (as indicated by a change in binding potential relative to non-displaced radioligand, or ΔBPND) appears to taper off in all or most of the constructs assessed. The authors should take care to point out that the decline in peak expression should not be confused with the decline in longitudinal expression, as this is not clear in the discussion; i.e. the subheading, "Factors influencing DREADD expression," might be better written as, "Factors influencing peak DREADD expression," and subsequent wording in this section should specify that these particular data concern peak expression only.
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Reviewer #3 (Public review):
Summary
This manuscript, from the developers of the novel DREADD-selective agonist DCZ (Nagai et al., 2020), utilizes a unique dataset where multiple PET scans in a large number of monkeys, including baseline scans before AAV injection, 30-120 days post-injection, and then periodically over the course of the prolonged experiments, were performed to access short- and long-term dynamics of DREADD expression in vivo, and to associate DREADD expression with the efficacy of manipulating the neuronal activity or behavior. The goal was to provide critical insights into the practicality and design of multi-year studies using chemogenetics and to elucidate factors affecting expression stability.
Strengths are systematic quantitative assessment of the effects of both excitatory and inhibitory DREADDs, quantification of both the short-term and longer-term dynamics, a wide range of functional assessment approaches (behavior, electrophysiology, imaging), and assessment of factors affecting DREADD expression levels, such as serotype, promoter, titer (concentration), tag, and DREADD type.
Minor weaknesses are related to a few instances of suboptimal phrasing, and some room for improvement in time course visualization and quantification. These would be easily addressed in a revision.
These findings will undoubtedly have a very significant impact on the rapidly growing but still highly challenging field of primate chemogenetic manipulations. As such, the work represents an invaluable resource for the community.
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Author response:
Public Reviews:
Reviewer #1 (Public review):
Overall, the conclusions of the paper are mostly supported by the data but may be overstated in some cases, and some details are also missing or not easily recognizable within the figures. The provision of additional information and analyses would be valuable to the reader and may even benefit the authors' interpretation of the data.
We thank the reviewer for the thoughtful and constructive feedback. We are pleased that the reviewer found the overall conclusions of our paper to be well supported by the data, and we appreciate the suggestions for improving figure clarity and interpretive accuracy. Below we address each point raised:
The conclusion that DREADD expression gradually decreases after 1.5-2 years is only based on a select few of the subjects assessed; in Figure 2, it appears that only 3 hM4Di cases and 2 hM3Dq cases are assessed after the 2-year timepoint. The observed decline appears consistent within the hM4Di cases, but not for the hM3Dq cases (see Figure 2C: the AAV2.1-hSyn-hM3Dq-IRES-AcGFP line is increasing after 2 years.)
We agree that our interpretation should be stated more cautiously, given the limited number of cases assessed beyond the two-year timepoint. In the revised manuscript, we will clarify in both the Results and Discussion that the observed decline is based on a subset of animals. We will also state that while a consistent decline was observed in hM4Di-expressing monkeys, the trajectory for hM3Dq expression was more variable—with at least one case showing increased in signal beyond two years.
Given that individual differences may affect expression levels, it would be helpful to see additional labels on the graphs (or in the legends) indicating which subject and which region are being represented for each line and/or data point in Figure 1C, 2B, 2C, 5A, and 5B. Alternatively, for Figures 5A and B, an accompanying table listing this information would be sufficient.
We thank the reviewer for these helpful suggestions. In response, we will revise the relevant figures as noted in the “Recommendations for the authors”, including simplifying visual encodings and improving labeling. We will also provide a supplementary table listing the animal ID and brain regions for each data point shown in the graphs.
While the authors comment on several factors that may influence peak expression levels, including serotype, promoter, titer, tag, and DREADD type, they do not comment on the volume of injection. The range in volume used per region in this study is between 2 and 54 microliters, with larger volumes typically (but not always) being used for cortical regions like the OFC and dlPFC, and smaller volumes for subcortical regions like the amygdala and putamen. This may weaken the claim that there is no significant relationship between peak expression level and brain region, as volume may be considered a confounding variable. Additionally, because of the possibility that larger volumes of viral vectors may be more likely to induce an immune response, which the authors suggest as a potential influence on transgene expression, not including volume as a factor of interest seems to be an oversight.
We thank the reviewer for raising this important issue. We agree that injection volume is a potentially confounding variable. In response, we will conduct an exploratory analysis including volume as an additional factor. We will also expand the Discussion to highlight the need for future systematic evaluation of injection volume, especially in relation to immune responses or transduction efficiency in different brain regions.
The authors conclude that vectors encoding co-expressed protein tags (such as HA) led to reduced peak expression levels, relative to vectors with an IRES-GFP sequence or with no such element at all. While interesting, this finding does not necessarily seem relevant for the efficacy of long-term expression and function, given that the authors show in Figures 1 and 2 that peak expression (as indicated by a change in binding potential relative to non-displaced radioligand, or ΔBPND) appears to taper off in all or most of the constructs assessed. The authors should take care to point out that the decline in peak expression should not be confused with the decline in longitudinal expression, as this is not clear in the discussion; i.e. the subheading, "Factors influencing DREADD expression," might be better written as, "Factors influencing peak DREADD expression," and subsequent wording in this section should specify that these particular data concern peak expression only.
We appreciate this important clarification. In response, we will revise the title to “Factors influencing peak DREADD expression levels”, and we will specify that our analysis focused on peak ΔBP<sub>ND</sub> values around 60 days post-injection. We will also explicitly distinguish these findings from the later-stage changes in expression seen in the longitudinal PET data in both the Results and Discussion sections.
Reviewer #2 (Public review):
Weaknesses
This study is a meta-analysis of several experiments performed in one lab. The good side is that it combined a large amount of data that might not have been published individually; the downside is that all things were not planned and equated, creating a lot of unexplained variances in the data. This was yet judiciously used by the authors, but one might think that planned and organized multicentric experiments would provide more information and help test more parameters, including some related to inter-individual variability, and particular genetic constructs.
We thank the reviewer for bringing this important point to our attention. We fully agree that the retrospective nature of our dataset, compiled from multiple studies conducted within a single laboratory, introduces variability due to differences in constructs, injection sites, and timelines. While this reflects the real-world constraints of long-term NHP research, we acknowledge the need for more standardized approaches. We will add a statement in the revised Discussion emphasizing that future multicenter and harmonized studies would be valuable for systematically examining specific parameters and inter-individual variability.
Reviewer #3 (Public review):
Minor weaknesses are related to a few instances of suboptimal phrasing, and some room for improvement in time course visualization and quantification. These would be easily addressed in a revision.
These findings will undoubtedly have a very significant impact on the rapidly growing but still highly challenging field of primate chemogenetic manipulations. As such, the work represents an invaluable resource for the community.
We thank the reviewer for the positive assessment of our manuscript and for the constructive suggestions noted in the “Recommendations for the authors”. In response, we will carefully review and revise the manuscript to improve visualization and quantification.
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- Mar 2025
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Author response:
The following is the authors’ response to the original reviews
Recommendations for the authors:
Reviewer #1 (Recommendations for the Authors):
The interpretation of results obtained with opto-Treacle (related to Figure 2C) may be expanded.
We thank the reviewer for their insightful comment regarding the interpretation of the results obtained with opto-Treacle. We understand the concern that the difference in the size of the condensates formed by opto-Treacle (Figure 2C) compared to Treacle-2S or other constructs may raise questions about the role of tetramerization in driving condensate formation, as 2S is known to tetramerize while FusionRed is not susceptible to multimerization.
To address this concern, we emphasize that we have demonstrated that overexpressed Treacle forms large condensates even in the absence of any fluorescent protein, as included in the revised manuscript. This observation supports the conclusion that Treacle's ability to form condensates is intrinsic and does not depend on the multimerization capacity of the fluorescent tag.
We believe that the observed difference in condensate size between opto-Treacle and Treacle-2S, Treacle-GFP, or untagged Treacle arises primarily from the time available for condensate assembly. Opto-Treacle condensation occurs rapidly, within approximately 10 seconds of blue light illumination, whereas Treacle-2S, Treacle-GFP, or untagged Treacle undergo condensation over the extended period of 24–48 hours of protein overexpression. This temporal difference likely accounts for the disparity in condensate size, as longer assembly times allow for larger and more mature condensates to form.
Given this reasoning, we consider it unnecessary to further emphasize the size differences in the main text of the article, as we believe the underlying explanation is clear and supported by the data. Nonetheless, we are open to incorporating additional clarifications if the reviewer deems it necessary.
The authors might reconsider referring to Treacle as a scaffold. Ultimately, the scaffold for the nucleolus is the rDNA with its bound proteins. Scaffold proteins, by definition, bind multiple protein partners and facilitate the formation of multiprotein complexes, a role not really attributed to homotypic LLPS.
We thank the reviewer for raising this important point regarding the use of the term "scaffold" in relation to Treacle. We fully acknowledge that rDNA, along with its associated protein complexes, serves as the primary structural scaffold for the nucleolus. However, we believe that referring to Treacle as a scaffold is appropriate and justified within the specific context of our study.
First, we emphasize that we describe Treacle as a scaffold specifically for nucleolar fibrillar centers (FCs), rather than for the nucleolus as a whole. This distinction is important, as our work focuses on the role of Treacle in organizing FC components, rather than the broader structural organization of the nucleolus.
Second, as the reviewer notes, scaffold proteins are defined by their ability to bind multiple protein partners and facilitate the formation of multiprotein complexes. Our findings demonstrate that Treacle's condensation properties promote the binding and retention of key rDNA-associated protein partners, including RPA194, UBF, and Fibrillarin, within the FCs. This activity aligns with the functional definition of a scaffold protein, as Treacle supports the spatial organization and cooperative interactions of FC components essential for rRNA transcription and processing. Therefore, while we appreciate the reviewer's observation regarding the central role of rDNA as a nucleolar scaffold, we maintain that the use of the term "scaffold" to describe Treacle's role in organizing FCs is consistent with its demonstrated functional properties.
If authors decide to add the "Ideas and Speculation" subsection to their Discussion, it may be interesting to discuss the following outstanding questions: does Treacle undergo homotypic or heterotypic LLPS? Does its overexpression favor homotypic interactions? How does it segregate FC and DFC compartments -by exclusion? How does phase-separated Treacle interact with other proteins?
We thank the reviewer for these insightful questions. While we believe that adding a dedicated "Ideas and Speculation" subsection would be redundant, we have already addressed the questions regarding Treacle’s homotypic or heterotypic LLPS and its interactions with other proteins in the revised "Discussion" section. Additionally, we have included a new section in the manuscript specifically focused on investigating the role of Treacle condensation in its interactions with protein partners, further expanding on these points.
In Materials and Methods, smFISH section -"probes were designed as described (Yao et al, 2019) and labeled with FITS on the 3'ends" - was it meant to say FITC (i.e. Fluorescein)?
We thank the reviewer for catching this error. This was indeed a typo, and we have corrected it to "FITC (i.e., Fluorescein)" in the revised text.
Reviewer #2 (Recommendations for the Authors):
Regarding recombinant Treacle, the main concern is that the authors may not be observing the condensation of Treacle itself. The quality of the purchased recombinant Treacle is unclear (this reviewer could not find Treacle listed on the vendor website despite using the supplied catalog number or vapors search terms). Furthermore, it is not clear if the condensates observed are Treacle or potentially the Dextran crowder. Only small percentages (>1%-5%) of either Dextran or PEG are needed to induce phase separation in two-component mixtures of these polymers. PEG may be in the Treacle storage butter. In addition to clarifying the State of recombinant Treacle, these concerns could be further assuaged by direct visualizing of Treacle forming condensates (via fluorescent n-terminal tagging) and filling in more of the phase space to observe the loss of condensates at a threshold concentration of Treacle. In general, the gold standard for establishing condensation of a given protein is mapping the full binodal phase diagram diagram of the protein. Understanding that protein is a limited resource, most groups simply map the lower concentration arm of the binodal, and this is sufficient to characterize a protein as having intrinsic condensation behavior. A similar mapping effort of Treacle would be welcomed.
We thank the reviewer for their thoughtful comments and for highlighting concerns regarding the interpretation of our experiments with commercial recombinant Treacle. We recognize the importance of ensuring that the observed condensation properties are intrinsic to Treacle and not influenced by potential contaminants, storage buffer components, or tags on the protein.
To address these concerns, we have re-evaluated the condensation properties of Treacle using a recombinant fragment independently purified in our laboratory. Specifically, we expressed and purified a Treacle fragment (amino acids 291–426), which includes two S/E-rich low-complexity regions (LCRs) and two linker regions, in E. coli. The protein was expressed as a TEV-cleavable maltose-binding protein (MBP) fusion, purified under native conditions via amylose resin, and subjected to TEV cleavage. This was followed by ion-exchange chromatography and extensive dialysis to remove any remaining impurities. These additional steps ensured that the purified Treacle fragment was of high purity and free from confounding components, such as polyethylene glycol (PEG). We have included detailed descriptions of this protocol in the revised manuscript.
Using this purified Treacle fragment, we confirmed its intrinsic condensation behavior in vitro. In the presence of 5% PEG8000 as a crowding agent, the fragment formed liquid-like condensates that exhibited spherical morphology and dynamic fusion events, key hallmarks of liquid-liquid phase separation (LLPS). Additionally, we demonstrated that the condensation of this Treacle fragment was sensitive to changes in pH and salt concentration but unaffected by 1,6-hexanediol treatment, suggesting that the condensates are stabilized predominantly by electrostatic interactions (Fig. 4B of the revised manuscript). Importantly, these findings provide robust evidence that Treacle possesses intrinsic phase-separation properties. All results from the commercial Treacle protein used in the initial version of the manuscript have been replaced with data obtained using this independently purified recombinant fragment.
We undestand that the condensation behavior of the fragment may not fully capture the behavior of full-length Treacle. Nevertheless, the in vitro experiments provide valuable mechanistic insights into the biophysical properties of Treacle. Furthermore, as emphasized in the revised manuscript, our study primarily focuses on understanding the condensation and functional role of Treacle in a cellular context, where we observe its critical involvement in organizing nucleolar structure and regulating rRNA transcription. These cellular experiments highlight the biological relevance of Treacle’s condensation behavior.
With regard to mapping the binodal phase diagram of Treacle, we concur with the reviewer that such an effort would be ideal for a more comprehensive characterization of Treacle’s condensation properties. However, the limited availability of purified protein currently precludes a detailed mapping effort. Despite this limitation, we believe the qualitative assessments of Treacle’s condensation under varying conditions, now included in the revised manuscript, sufficiently demonstrate its intrinsic ability to phase-separate.
In conclusion, we are grateful for the reviewer’s feedback, which has allowed us to refine our methodology and strengthen the evidence supporting the intrinsic condensation properties of Treacle. We are confident that the revised manuscript provides a robust and thorough characterization of Treacle’s phase-separation behavior and its functional role in the cell, addressing the reviewer’s concerns. Thank you for your constructive recommendations, which have significantly improved the quality of our work.
Replacing 'liquid-phase' and 'liquid' with 'liquid-like' would make the language consistent with other papers in the field and more accurately reflect the degree of material state analysis carried out in the study.
We thank the reviewer for this insightful recommendation. In response to the suggestion, we have revised the manuscript to replace the terms "liquid-phase" and "liquid" with "liquid-like" throughout the text. This change ensures consistency with terminology commonly used in the field and more accurately reflects the degree of material state analysis performed in our study. We believe this adjustment improves the clarity and precision of our findings, aligning the manuscript with standard practices in the field. Thank you for helping us enhance the quality of the presentation.
The 'unclear' nature of the condensation behavior of the FC phase of the nucleolus is listed as a motivation for carrying out the study in the introduction; the authors could note here two recent papers that have investigated the nature of FC condensation: Jaberi-Lashkari et al. 2023 and King et al. 2024. The reviewer notes that while these were both pre-printed in late 2022, they were only recently published.
We thank the reviewer for bringing these recent studies to our attention. In response to the suggestion, we have cited the papers by Jaberi-Lashkari et al. (2023) and King et al. (2024) in both the introduction and discussion sections of the revised manuscript. These references are highly relevant to the context of our study and provide valuable insights into the condensation behavior of the FC phase of the nucleolus. We agree that incorporating these works strengthens the framing of our study and situates it more effectively within the broader field. Thank you for this constructive recommendation.
The statement that Treacle is "the main molecule present in the FC" is a substantial claim that does not need to be made to promote the author's case, nor is it well supported by the provided reference (Gal et al., 2022).
We thank the reviewer for pointing out this overstatement in our original manuscript. In response, we have revised the text to provide a more accurate and well-supported description. Specifically, we have replaced the claim that Treacle is "the main molecule present in the FC" with a statement highlighting its direct interactions with UBF and RNA Pol I, as well as its colocalization with these proteins within the FC. This revision ensures alignment with the provided references and more accurately reflects the current understanding of Treacle's role in the FC. We appreciate the reviewer's attention to this detail, which has helped us improve the clarity and accuracy of our manuscript.
The statement that "Treacle is one of the most intrinsically disordered proteins" is vague and unnecessarily grand. Treacle is a fully intrinsically disordered protein; these comprise 5% of the human proteome (Tsang et al. 2020), so Treacle is, indeed, unusual in that regard.
We thank the reviewer for highlighting the vague and unnecessarily broad nature of the original statement. In response, we have revised the text to provide a more precise and accurate description of Treacle's structural properties. Specifically, we replaced the claim that "Treacle is one of the most intrinsically disordered proteins" with the statement that "According to protein structure predictors (e.g., AlphaFold, IUPred2, PONDR, and FuzDrop), Treacle is a fully intrinsically disordered protein." This wording reflects the unique nature of Treacle while remaining scientifically accurate and supported by reliable computational predictions. We appreciate the reviewer's feedback, which has allowed us to improve the rigor and clarity of our manuscript.
A comment on the implications of the immobile pool of Treacle (which appears to be ~50% in WT and across a range of mutants) would be welcome. Additionally, the limitations of FRAP for interrogating material properties of condensed material in living systems are provided in Goetz and Mahamid, 2020. In this paper, the authors review instances where the ultrastructure of condensate is known and where FRAP data is available. They show that crystalline assemblies can recover faster than apparently liquid, spherical assemblies. A comment in the text about how these limitations apply to this study would be welcome.
We appreciate the reviewer’s insightful comments regarding the interpretation of the immobile pool of Treacle and the limitations of FRAP for characterizing material properties in living systems. As noted in our response to the public review, we believe the ~50% recovery rate after photobleaching observed in our experiments is best explained by the redistribution of Treacle molecules within the condensate, rather than significant exchange with the surrounding phase. This interpretation is strongly supported by the full- and half-FRAP analyses included in the revised manuscript, which demonstrated internal mixing dynamics within the condensates.
There appears to be a typo in the following sentence: "The highly positively charged CD serves as the nucleation center for RD but exhibits ambivalent phase properties, transitioning from LLPS to LSPS in the absence of rRNA." The LLPS to LSPS behavior was observed for mutants to the central domain (RD), not the c-terminal domain (CD).
Throughout the authors report single snapshots of representative cells and single line traces. Analysis of the key morphological feature across the population of cells would help the reader understand how widespread the observed phenotype is.
We thank the reviewer for raising this important point regarding the representation of morphological features across the cell population. To address this concern, we have included widefield micrographs of cell fields in the revised figures to provide a more comprehensive view of the phenotypes observed.
The statement that "The phase behavior of polymers is determined by interactions through associative motifs, referred to as stickers, separated by spacers, which are not the primary driving forces for phase separation" could be improved by pointing out that this is potentially incomplete for describing the kind of condensation that highly charged polymers undergo. The high charge and charge segregation of Treacle suggest that it is a blocky polyampholyte and that it condenses by coacervation. Models of associative polymers can be useful for describing coacervation, however, the driving forces for coacervation are less understood and have been proposed to include an entropic component (see Sathyavageeswaran et al. 2024, Sing and Perry 2020 and work from their groups as well as the Obermayer (Columbia) and Terrell (U. Chicago) Groups).
We thank the reviewer for highlighting this important aspect of the phase behavior of charged polymers and for suggesting relevant references. In response, we have revised the discussion section of the manuscript to include a more nuanced explanation of the condensation mechanisms for highly charged polymers such as Treacle. Specifically, we now describe Treacle as a blocky polyampholyte, suggesting that its condensation behavior may be driven by coacervation mechanisms.The relevant references have been added to the discussion section of the revised manuscript.
In addition to the above, the authors may consider citing two recent publications from the Pappu group (King et al. Cell 2024 and King et al. Nucleus 2024) that directly investigate the condensation potential of K-rich and E/D-rich' grammars' on nucleolar proteins and show that, like the authors, the K-rich region is essential for localization and is conserved across nucleolar proteins.
We thank the reviewer for bringing these relevant publications to our attention. The suggested references from the Pappu group (King et al., Cell 2024, and King et al., Nucleus 2024) have been added to the introduction and discussion sections of the revised manuscript, and their findings have been appropriately integrated into our analysis.
The authors could consider replacing the use of LLPS with a more generic term such as "condensation" or "biomolecular condensation." LLPS of polymers is a segregative transition driven by its incompatibility with the surrounding solvent. As indicated, Treacle is likely to be undergoing some form of coacervation (which is predominantly an associative tradition), which can be genetically described as condensation. See Pappu et al. 2023 for more details.
We thank the reviewer for their insightful suggestion. Following the reviewer's recommendation, we have replaced the term "LLPS" with "condensation" or "coacervation" throughout the manuscript, where appropriate. Additionally, we have referenced Pappu et al. (2023) and other to provide further context and clarity regarding the distinctions between these terms.
The authors cite Yao et al. 2019, but do not cite the follow-up study (Wu et al. 2021) or provide a statement on how the Chan group finds a role for the RGG domain of FBL in keeping the certain canonical markers of the FC and DFC de-mixed.
We thank the reviewer for pointing out these important references. The relevant citations, including Wu et al. (2021), have been added to the manuscript.
Reviewer #3 (Recommendations for the Authors):
The following comment is true but could be broadened to include examples of structured regions promoting biomolecular condensation. "In biological systems, phase separation is mainly a characteristic of multivalent or intrinsically disordered proteins (Banani et al, 2017; Shin & Brangwynne,2017; Uversky, 2019)."
We have expanded the statement as recommended by the reviewer: "In biological systems, phase separation is facilitated by a combination of multivalent interactions mediated by intrinsically disordered proteins and site-specific interactions that drive percolation."
Related to Figure 1.
The authors report Treacle-dependent EU incorporation (Figure 1D), but are there any changes more broadly to nucleolar number or size as a consequence? How do the authors interpret that the quantitative effect of AMD treatment is more extreme than Treacle depletion (Figure 1E).
We thank the reviewer for raising these important points. Regarding nucleolar number and morphology, we did not observe a change in the number of nucleoli upon Treacle depletion. However, nucleoli appeared more regularly rounded under these conditions, which we interpret as a consequence of the decreased rDNA transcription activity caused by Treacle depletion. A similar rounding of nucleoli is also observed upon actinomycin D (AMD) treatment, which is consistent with reduced transcriptional activity.
As for the more pronounced effect of AMD compared to Treacle depletion on EU incorporation, this can be explained by the fundamentally different mechanisms through which these conditions affect transcription. Treacle depletion reduces the local concentration of transcription factors at rDNA sites, thereby impairing transcription initiation and elongation to a certain extent. However, under Treacle depletion, RNA polymerase I still retains the ability to bind to the promoter and support a residual level of transcription. In contrast, AMD acts as a potent intercalator in GC-rich regions of rDNA, physically blocking the ability of RNA polymerase I to move along rDNA, resulting in near-complete cessation of rRNA synthesis.
Related to Figure 2.
The authors observe that AMD leads to coalescence of individual Treacle-2S+ bodies (e.g. Figure 2E) - does this suggest that ongoing rRNA transcription is required to prevent such events?
Thank you for your thoughtful question. Indeed, our observations strongly suggest that ongoing rRNA transcription is required to prevent the coalescence of Treacle-2S+ bodies, as observed upon AMD treatment. This interpretation aligns with the findings of Tetsuya Yamamoto et al., who demonstrated that nascent ribosomal RNA (pre-rRNA) acts as a surfactant to suppress the growth and fusion of fibrillar centers (FCs) in the nucleolus. Their work highlighted that nucleolar condensates formed via liquid-liquid phase separation (LLPS) tend to grow to minimize surface energy, provided sufficient components are available. However, the transcription of prerRNA stabilizes FCs by maintaining multiple microphases, preventing coalescence unless transcription is inhibited.
According to Yamamoto et al., nascent pre-rRNAs tethered to FC surfaces by RNA Polymerase I generate lateral pressure that counteracts interfacial tensions, effectively suppressing FC fusion. This activity is analogous to the surfactant properties of molecules in physical systems. When transcription is inhibited (e.g., by AMD), the loss of nascent rRNA allows condensates to coalesce, consistent with the behavior we observe.
We further propose that the AMD-induced coalescence of Treacle-2S+ bodies reflects the loss of this surfactant-like effect, as transcriptional activity ceases. This theory is also supported by the observation that Treacle condensates in the nucleoplasm, where rRNA transcription is absent, form larger structures. Collectively, these insights highlight the critical role of ongoing rRNA transcription in maintaining the structural integrity and dynamic organization of nucleolar substructures.
Related to Figure 3.
In the figure panels B-H the DAPI signal in gray obscures the Treacle localization, especially in Figure 3H. A non-merged image for each of these examples for the Treacle localization would be very helpful.
We thank the reviewer for this observation. To address this, we have included wide-field images without the DAPI overlay for the deletion mutant lacking the 1121-1488 region. These are now presented in Supplementary Figure S5G of the revised manuscript.
Related to Figure 5.
Only a single representative nucleus is shown in the PLA analysis presented in Figure 5B.
Quantification to assess the robustness of this response with the addition of VP16 is needed. The authors use ChIP and immunocytochemistry as orthogonal methods but it would be best to therefore show both for each manipulation that is performed - the immunostaining of TOPBP1 in the Treacle KD cells in S5A should be in the main Figure 5 to complement transformation of constructs as in Figure 5D.
We appreciate the reviewer’s comment. To address this, we performed a quantitative analysis of PLA fluorescence signals in control and etoposide-treated cells, and the results are now presented in Supplementary Figure S8C. Additionally, as recommended, we have transferred the results of the immunocytochemistry of TOPBP1 in Treacle KD and Treacle KN cells to the main figure, now included as Figures 7D-E in the revised manuscript.
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Author response:
The following is the authors’ response to the original reviews
Reviewer #3 (Recommendations for the authors):
Major concerns:
P.6, lines 223-224: The sentence sounds like the authors produced all the OVGP1s by themselves in their laboratories, which is not completely true. The recombinant human and mouse OVGP1s were purchased from OriGene. It is suggested that the authors should state and explain clearly here which OVGP1 is produced by their laboratories and that recombinant human and mouse OVGP1s were obtained and purchased from Origene.
It is already clearly included in the M&M.
P6, lines 227-229: The authors stated that "Western blots of the three OVGP1recombinants indicated expected sizes based on those of the proteins: 75 kDa for human and murine OVGP1 and around 60 kDa for bovine OVGP1 (Fig. 4B and S6)." I pointed out in my last review report that the size of the recombinant human OVGP1shown by the authors in their manuscript is not in agreement with what has been published previously in literature regarding the molecular weight of native human OVGP1 as well as that of recombinant human OVGP1. The authors did not address the above concern adequately. In fact, recombinant human OVGP1 has been produced a few years ago (Reproduction (2016) 152:561-573) and it has been previously demonstrated that a single protein band of approximately 110-130 kDa was detected for both native human OVGP1 (see Microscopy Research and Technique (1995) 32:57-69) and recombinant human OVGP1 (Reproduction (2016) 152:561-573; Carbohydrate Research (2012) 358:47-55) using antibodies specific for human OVGP1. Molecular weight of the protein core or polypeptide of human OVGP1 is approximately 75 kDa, but the glycosylated form of native human OVGP1 and recombinant human OVGP1 is approximately 110-130 kDa. Therefore, the authors might have been using the recombinant core protein of human OVGP1 instead of the fully glycosylated recombinant OVGP1 in their study. The same concern also applies to the commercially obtained mouse recombinant OVGP1 used by the authors in their study. I would also like to mention that the mature and fully glycosylated OVGP1s in mammals vary in molecular weight (90-95 kDa in domestic animals; 110-150 kDa in primates; 160-350 kDa in rodents). Again, the 75kDa of mouse OVGP1 detected by the authors could be the core protein or polypeptide of mouse OVGP1 instead of the fully glycosylated mouse OVGP1.
In our study, as previously mentioned, we included commercially available recombinant proteins from Origene for human and murine OVGP1, which are produced in mammalian cells, and we also produced and purified bovine OVGP1 in mammalian cells. Therefore, these proteins should be properly glycosylated. Moreover, we performed Western blot assays favouring the blotting of higher molecular weight proteins, ensuring the optimal conditions for the assay. Additionally, we tested the size of OVGP1 from murine and bovine oviductal fluids on the same blot. During oestrus, the size of OVGP1 from oviductal fluids matches that of the recombinant proteins, and this band is downregulated during anoestrus, confirming the proper size of recombinant protein.
P.7, lines 236 and 237: Please provide a figure or source to support the statement "...as confirmed by proteomics of the bands along with PEAKS Studio v11.5 search engine peptide identification software."
It is included in the text the amount of unique peptides obtained by Proteomics for OVGP1 identification over all protein groups identified.
P.7, lines 243 to 245: The statement "...using rabbit polyclonal antibody to human OVGP1 for bOVGP1 and endogenous OVGP1, and mouse monoclonal antibody against Flag (DDK)-tag for hOVGP1 and mOVGP1." is confusing and might be inaccurate. First of all, I wondered why the authors did not use an antibody against bovine OVGP1 for the recombinant bOVGP1 instead of using a rabbit polyclonal antibody to human OVGP1. Secondly, what does the "endogenous OVGP1" refer to in the statement? Thirdly, the authors in their study used the commercially available recombinant human OVGP1 and recombinant mouse OVGP1 purchased from Origene. Based on the data sheet provided by Origene, the tag used for both recombinant human OVGP1 and recombinant mouse is C-Myc/DDK-tag and not Flag-tag. Can the authors explain these discrepancies?
Firstly, for the recombinant protein of bOVGP1 we used the same antibody that we used in the Western blot for all the proteins and oviductal fluids because we do not have anti-His tag working for Immunofluorescence (the one we had only worked for Western blot) and neither we do not have any antibody against bovine OVGP1. In the case of human and murine since we had anti-Flag antibody that worked for Western blot and for immunofluorescence, we used this one. However, as has been shown in our figure and supplementary material, the antibody against human OVGP1 works properly for both techniques (Western blot and Immunofluorescence). Secondly, endogenous OVGP1 is referred to the OVGP1 present in the oviductal fluid. Thirdly, as you can see in the datasheet of the protein, the recombinant proteins purchased from Origene contains a c-myc tag (EQKLISEEDL) some amino acids and a ddk-tag (DYKDDDDK). The sequence of ddk is the same of Flag-tag (DYKDDDDK). Since the proteins have both tags we used the antibody against Flag (or ddk) epitope.
P12, lines 429-432: The newly added statement at the end of the Discussion saying "Additionally, future studies would be valuable to investigate whether incubating oocytes with oviductal fluid (or OVGP1) could reduce polyspermy in porcine IVF and whether ZPs could be leveraged to naturally enhance sperm selection in human ICSI" is very concerning and requires further attention. The statement reflects that the authors do not keep pace with and do not pay attention to what has been published in literature regarding porcine and human OVGP1s. In fact, porcine oviduct-specific glycoprotein (OVGP1) has already been reported to reduce the incidence of polyspermy in pig oocytes (Biology of Reproduction (2000) 63:242-250). Porcine oviductal fluid, used in porcine IVF, has also been found to exert a beneficial effect on oocytes by reducing the incidence of polyspermy without decreasing the penetration rate. (Theriogenology (2016) 86:495-502). Therefore, the studies deemed valuable by the authors to be investigated in the future have, in fact, already been carried out two decades ago by several other laboratories. I am surprised the authors were not aware of these published work in literature. All the above should have been incorporated in the Discussion.
This sentence is modified in the discussion and the references are included.
Furthermore, as mentioned earlier, recombinant human OVGP1 has also been produced (Reproduction (2016) 152:561-573), and recombinant human OVGP1 has been found to increase tyrosine phosphorylation of sperm proteins, a biochemical hallmark of sperm capacitation, and potentiate the subsequent acrosome reaction (Reproduction (2016) 152:561-573) as well as increase sperm-zona binding (Journal of Assisted Reproduction and Genetics (2019) 36:1363-1377). These earlier findings should be incorporated into the Discussion.
Thank you for your comment, but in this work we had not performed any experimental setting related to tyrosine phosphorylation and despite is a very interesting topic is not directly related to this work.
P.19, lines 678-683: Since the human and mouse recombinant oviductin proteins were purchased from Origene, the authors should be aware of the fact that these commercially available recombinant OVGP1s might not be fully glycosylated. While I appreciate the fact that the authors wanted to briefly describe how the human and mouse recombinant OVGP1s were prepared by the manufacturer, I strongly suggest that the authors should contact Origene, the manufacturer, for all information regarding the procedures for producing the human and mouse recombinant oviductin proteins. For example, the authors stated on lines 680-681 that "A sequence expressing FLAG-tagged epitope proteins (DYKDDDDK) was cloned into an expression vector." According to the data sheet provided by Origene, it appears that both human and recombinant oviductin proteins are C-Myc/DDK-tagged and not FLAG-tagged.
Thank you for your comment, as according to the sequence of Flag-tag it is matching with the sequence of the tag in the datasheet corresponding to DDK (this is in detail in previous comment). Besides, the protein is tagged also by C-Myc tag. Among both tags, the antibody selected to detect it was anti-Flag tag.
P.19, lines 692-697: The description of the primary and secondary antibodies used for detection of the various recombinant OVGP1s is also very confusing and not clearly presented. For example, it is mentioned here that "...membranes were...incubated with anti-OVGP1 rabbit monoclonal antibody for OVGP1,..". What specifically does "OVGP1" refer to here? The authors then stated that anti-Histamine Tag antibody was used to detect bOVGP1 and mOVGP1 and anti-Flag antibody was used to detect hOVGP1. As pointed out earlier, the human and mouse recombinant OVGP1s were produced using C-Myc/DDK tag and not His-tag or Flag-tag. Can the authors clarify these discrepancies?
We apologise for the complexity of the antibodies, we included in this paragraph the ones used to Western blot for both figures: anti- human OVGP1 was used for the principal figure that contains the three recombinant proteins and oviductal fluids; and the anti-Histidine and anti-Flag antibodies that are included in supplementary figure, specifically for recombinant bovine OVGP1 (Histidine tag) and for recombinant murine and human OVGP (DDK tag). A clarifying sentence has been included in the text.
P.31, lines 1143-1149: Figure 10 is not mentioned anywhere in the main text of the manuscript. Rewrite the second half of the sentence "...; being this specificity lost when OVGP1 is heterologous to the ZP (right diagram)." Which sounds awkward and grammatically not correct.
The figure is already mentioned in the text, thank you for your comment. The sentence is also corrected.
Other comments: P.1, the statement of "All authors contributed equally to this work" on line 14 can be deleted because detailed and specific contributions from each authors are listed in lines 1009-1017 on page 27.
Both authors contributed equally to this work, now is clear in authors contribution section.
P.2, lines 43 and 44: Do the authors mean "sperm-oocyte binding protein" instead of "sperm-oocyte fusion protein" in the sentence? "Fusion protein" is a protein composed of two or more domains encoded by different genes, or a hybrid molecule created by combining two different proteins for various purposes. I believe the term "fusion protein" is wrongly used in the sentence which should be rephrased with a proper term.
Done.
P2, line 73: Remove the comma after the word "Both".
Done.
P.5, line 179: "...mice ZP..." should be written as "...mouse ZP...".
Done.
P.6, heading of 3rd paragraph on line 207: The term "binding" will be a better term than "fusion" used in the heading because the results do not actually show the fusion of the OVGP1 proteins with the ZP glycoprotein. Instead, binding of the OVGP1 proteins to the ZP occurred.
Done.
P.6, lines 215-217: Authors, please provide a reference or references to support the statement "Region A, corresponding to the amino acid end, shows high identity among monotremes, marsupials and placentals."
In the text was indicated a review (29) which includes the supporting idea of this statement for Figure 4. Moreover, we have included some if the references used for the description of the domains when performing the sequence alignment of Figure S5.
P.6, line 230 and line 233 on P.7: Authors, please be consistent in the use of either American English or British English. The word "oestrus" is British English whereas "estrus" is American English.
Done.
P.7, line 264: The word "sticking" used here means non-specific binding. I believe the author means specific binding here. If so, a more appropriate word should be used here instead of "sticking".
Done.
P.7, lines 267-269: This newly added sentence sounds very awkward and should be completely rewritten.
Done.
P.8, line 288: This reviewer finds it difficult to understand the meaning of the heading. The heading should be rephrased to bring out exactly what the authors want to say in well-written English.
Done.
P.8, line 290: The word "would" should be replaced by "could" in the sentence.
Done.
P.13, line 437: Authors, please provide the location of Sigma-Aldrich.
Done.
P.13, line 457: Here, the authors used "1800 rpm" to indicate the centrifugation speed but used the g-force elsewhere in the Materials and Methods. Please be consistent. The g-force is preferred.
Done.
P.14, lines 483-485: The procedure of sacrificing the cats should be provided in the Materials and Methods
Cats weren’t sacrificed they were vasectomized. It is now included in the text.
P.17, line 628: "...the ZPs were exposed or no exposed to..." should be written as "...the ZPs were either exposed or not exposed to...".
Done.
P.17, line 629: "...each groups were incubated with..." should be "...each group was incubated with...".
Done.
P.19, line 700: "As loading control, was used the primary antibody....." is not a complete sentence and it needs to be rewritten.
Done.
P.20, lines 744-754: For scanning electron microscopy and image processing, the procedures of prior treatment of the oocytes with and without oviductal fluid and OVGP1 should be included here.
Done.
P.21, line 756: It is stated here that "Two hundred isolated ZPs were treated with Clostridium perfringens neuraminidase....". However, it is not clear whether two hundred isolated ZPs of both porcine and murine ZPs were treated. Authors, please clarify.
We used 200 isolated ZPs of each specie, bovine and murine. It is classified in the text.
P.28, lines 1039 and 1040: The author only mentioned the use of bovine and murine sperm here. What about human sperm?
Done.
P.29, line 1076: "...in mammalian cells..." is very vague. Be specific what exactly the mammalian cells were.
Done.
P.29, line 1079: "Oviductal fluid from ovulated cows or anoestrus cows." is not a complete sentence and it needs to be rewritten.
Done.
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Author response:
The following is the authors’ response to the original reviews
eLife Assessment
In this valuable study, García-Vázquez et al. provide solid evidence suggesting that G2 and S phases expressed protein 1 (GTSE1), is a previously unappreciated non-pocket substrate of cyclin D1-CDK4/6 kinases. To this end, this study holds a promise to significantly contribute to an improved understanding of the mechanisms underpinning cell cycle progression. Notwithstanding these clear strengths of the article, it was thought that the study may benefit from establishing the precise role of cyclin D1-CDK4/6 kinase-dependent GTSE1 phosphorylation in the context of cell cycle progression, …
We do not claim, as editors and reviewers appear to have interpreted, that GTSE1 is phosphorylated by cyclin D1-CDK4 in the G1 phase of the cell cycle under normal physiologic conditions. Indeed, we agree with the existing literature indicating that in cells that do not express high levels of cyclin D1, GTSE1 is expressed predominantly during S and G2 phase (hence the name GTSE1, which stands for G-Two and S phases expressed protein 1) and is phosphorylated by mitotic cyclins in early mitosis. Even during G1, when the levels of cyclin D1 peak, GTSE1 is not phosphorylated in normal cells. This could be due to either a higher affinity between GTSE1 and mitotic cyclins as compared to D-type cyclins or to a higher concentration of mitotic cyclins compared to D-type cyclins. In the current manuscript, we show that higher levels of cyclin D1 can drive the sustained phosphorylation of GTSE1 across all cell cycle points. To reach this conclusion, we do not rely only on the overexpression of exogenous cyclin D1. In fact, we observe similar effect when we deplete endogenous AMBRA1, resulting in the stabilization of endogenous cyclin D1 in all cell cycle phases (see Figure 2G and Figure supplement 3B). As we had already mentioned in the Discussion section, we propose that GTSE1 is phosphorylated by CDK4 and CDK6 particularly in pathological states, such as cancers displaying overexpression of D-type cyclins (i.e., it is possible that the overexpression overcomes the lower affinity of the cyclin D-GTSE1 complex). In turn, phosphorylation of GTSE1 induces its stabilization, leading to increased levels that, as expected based on the existing literature, contribute to enhanced cell proliferation. So, the role of the cyclin D1-CDK4/6 kinase-dependent GTSE1 phosphorylation is to stabilize GTSE1 independently of the cell cycle. In sum, our study suggests that overexpression of cyclin D1, which is often observed in cancers cells beyond the G1 phase, induces phosphorylation of GTSE1 at all points in the cell cycle.
… obtaining more direct evidence that cyclin D1-CDK4/6 kinase phosphorylate indicated sites on GTSE1 (e.g., S454) …
We show that treatment of cells with palbociclib completely abolished the effect of cyclin D1-CDK4 on the GTSE1 shift observed using Phos-tag gels (Figure 2H). Moreover, mutagenesis analysis shows that S91, S262, and S724 are phosphorylated in a cyclin D1-CDK4-dependent manner (Figure 2F and Figure supplement 3A). Compared to wild-type GTSE1, a triple mutant (S91A/S262A/S724A) displayed loss of slower-migrating bands upon co-expression of cyclin D1-CDK4, suggesting diminished phosphorylation. Nevertheless, a residual slow-migrating band persisted, prompting further mutations of the triple GTSE1 mutant in S331 and S454 (individually), which do not have a CDK-phosphorylation consensus, but were identified in several published phospho-proteomics studies. From these two quadruple mutants, only the that containing the S454A mutation demonstrated a complete abrogation of any shift in phos-tagTM gels (Figure 2F). These studies suggest that four major sites (S91, S262, S454, and S724) are phosphorylated (either directly and/or indirectly) in a cyclin D1-CDK4-dependent manner.
… and mapping a degron in GTSE1 whose function may be blocked by cyclin D1-CDK4/6 kinase-dependent phosphorylation.
We show that stabilization or overexpression of cyclin D1, which is often observed in human cancers, promotes GTSE1 phosphorylation on S91, S262, S454, and S724, resulting in GTSE1 stabilization. Similarly, a phospho-mimicking mutant with the 4 serine residues replaced with an aspartate at positions 91, 261, 454, and 724 display increased half-life. While we appreciate the editor’s suggestion and agree on these being interesting questions, we would like to respectfully point out that mapping the GTSE1 degron and understanding how it is affected by cyclin D1-CDK4/6-dependent phosphorylation is outside the scope of the current project and will require an extensive set of experiments and tools. Accordingly, the three reviewers did not ask to map the GTSE1 degron. We plan on addressing these interesting questions as part of a follow-up study.
Reviewer #1 (public review):
Summary:
García-Vázquez et al. identify GTSE1 as a novel target of the cyclin D1-CDK4/6 kinases. The authors show that GTSE1 is phosphorylated at four distinct serine residues and that this phosphorylation stabilizes GTSE1 protein levels to promote proliferation.
Strengths:
The authors support their findings with several previously published results, including databases. In addition, the authors perform a wide range of experiments to support their findings.
Weaknesses:
I feel that important controls and considerations in the context of the cell cycle are missing. Cyclin D1 overexpression, Palbociclib treatment and apparently also AMBRA1 depletion can lead to major changes in cell cycle distribution, which could strongly influence many of the observed effects on the cell cycle protein GTSE1. It is therefore important that the authors assess such changes and normalize their results accordingly.
We have approached the question of GTSE1 phosphorylation to account for potential cell cycle effects from multiple angles:
(i) We conducted in vitro experiments with purified, recombinant proteins and shown that GTSE1 is phosphorylated by cyclin D1-CDK4 in a cell-free system (Figure 2A-C). These experiments provide direct evidence of GTSE1 phosphorylation by cyclin D1-CDK4 without the influence of any other cell cycle effectors.
(ii) We present data using synchronized AMBRA1 KO cells (new Figure 2G and Figure supplement 3B). In agreement with what we had shown previously (Simoneschi et al., Nature 2021, PMC8875297), AMBRA1 KO cells progress faster in the cell cycle but they are still synchronized as shown, for example, by the mitotic phosphorylation of Histone H3, peaking at 32 hours after serum readdition like in parental cells. Under these conditions we observed that while phosphorylation of GTSE1 in parental cells is evident in the last two time points, AMBRA1 KO cells exhibited sustained phosphorylation of GTSE1 across all cell cycle phases. This was evident enough when using Phos-tag gels as in the top panel of the old Figure 2G. We now re-run one the biological triplicates of the synchronized cells using higher concentration of Zn<sup>+2</sup>-Phos-tag reagent and lower voltage to allow better separation of the phosphorylated bands. Under these conditions, GTSE1 phosphorylation is better appreciable (top panel of the new Figure 2G). This experiment provides evidence that high levels of cyclin D1 in AMBRA1 KO cells affect GTSE1 phosphorylation independently of the specific points in the cell cycle.
(iii) The relative short half-life of GTSE1 (<4 hours) makes its levels sensitive to acute treatments such as Palbociclib or acute AMBRA1 depletion. The effects of these treatments on GTSE1 levels are measurable within a time frame too short to significantly affect cell cycle progression. For example, we used cells with fusion of endogenous AMBRA1 to a mini-Auxin Inducible Degron (mAID) at the N-terminus. This system allows for rapid and inducible degradation of AMBRA1 upon addition of auxin, thereby minimizing compensatory cellular rewiring. Again, we observed an increase in GTSE1 levels upon acute ablation of AMBRA1 (i.e., in 8 hours) (Figure 3B), when no significant effects on cell cycle distribution are observed (please see Simoneschi et al., Nature 2021, PMC8875297 and Rona et al., Mol. Cell 2024, PMC10997477).
Altogether, the above lines of evidence support our conclusion that GTSE1 is a target of cyclin D1-CDK4, independent of cell cycle effects.
In conclusion, we do not claim that GTSE1 is phosphorylated by cyclin D1-CDK4 in the G1 phase of the cell cycle under normal physiologic conditions. Indeed, we agree with the existing literature indicating that in cells that do not express high levels of cyclin D1, GTSE1 is expressed predominantly during S and G2 phase (hence the name GTSE1, which stands for G-Two and S phases expressed protein 1) and is phosphorylated by mitotic cyclins in early mitosis. Even during G1, when the levels of cyclin D1 peak, GTSE1 is not phosphorylated in normal cells. This could be due to either a higher affinity between GTSE1 and mitotic cyclins as compared to D-type cyclins or to a higher concentration of mitotic cyclins compared to D-type cyclins. In the current manuscript, we show that higher levels of cyclin D1 can drive the sustained phosphorylation of GTSE1 across all cell cycle points. To reach this conclusion, we do not rely only on the overexpression of exogenous cyclin D1. In fact, we observe similar effect when we deplete endogenous AMBRA1, resulting in the stabilization of endogenous cyclin D1 in all cell cycle phases (see Figure 2G and Figure supplement 3B). As we had already mentioned in the Discussion section of the original submission, we propose that GTSE1 is phosphorylated by CDK4 and CDK6 particularly in pathological states, such as cancers displaying overexpression of D-type cyclins (i.e., it is possible that the overexpression overcomes the lower affinity of the cyclin D1-GTSE1 complex). In turn, phosphorylation of GTSE1 induces its stabilization, leading to increased levels that, as expected based on the existing literature, contribute to enhanced cell proliferation. In sum, our study suggests that overexpression of cyclin D1, which is often observed in cancers cells beyond the G1 phase, induces phosphorylation of GTSE1 at all points in the cell cycle.
Reviewer #2 (public review):
Summary:
The manuscript by García-Vázquez et al identifies the G2 and S phases expressed protein 1(GTSE1) as a substrate of the CycD-CDK4/6 complex. CycD-CDK4/6 is a key regulator of the G1/S cell cycle restriction point, which commits cells to enter a new cell cycle. This kinase is also an important therapeutic cancer target by approved drugs including Palbocyclib. Identification of substrates of CycD-CDK4/6 can therefore provide insights into cell cycle regulation and the mechanism of action of cancer therapeutics. A previous study identified GTSE1 as a target of CycB-Cdk1 but this appears to be the first study to address the phosphorylation of the protein by Cdk4/6.
The authors identified GTSE1 by mining an existing proteomic dataset that is elevated in AMBRA1 knockout cells. The AMBRA1 complex normally targets D cyclins for degradation. From this list, they then identified proteins that contain a CDK4/6 consensus phosphorylation site and were responsive to treatment with Palbocyclib.
The authors show CycD-CDK4/6 overexpression induces a shift in GTSE1 on phostag gels that can be reversed by Palbocyclib. In vitro kinase assays also showed phosphorylation by CDK4. The phosphorylation sites were then identified by mutagenizing the predicted sites and phostag got to see which eliminated the shift.
The authors go on to show that phosphorylation of GTSE1 affects the steady state level of the protein. Moreover, they show that expression and phosphorylation of GTSE1 confer a growth advantage on tumor cells and correlate with poor prognosis in patients.
Strengths:
The biochemical and mutagenesis evidence presented convincingly show that the GTSE1 protein is indeed a target of the CycD-CDK4 kinase. The follow-up experiments begin to show that the phosphorylation state of the protein affects function and has an impact on patient outcomes.
Weaknesses:
It is not clear at which stage in the cell cycle GTSE1 is being phosphorylated and how this is affecting the cell cycle. Considering that the protein is also phosphorylated during mitosis by CycB-Cdk1, it is unclear which phosphorylation events may be regulating the protein.
Please see point (ii) and the last paragraph in the response to Reviewer #1. Moreover, we show that, compared to the amino acids phosphorylated by cyclin D1-CDK4, cyclin B1-CDK1 phosphorylates GTSE1 on either additional residues or different sites (Figure 2H). We also show that expression of a phospho-mimicking GTSE1 mutant leads to accelerated growth and an increase in the cell proliferative index (Figure 4B,C and new Figure supplement 4D-E). Finally, we have evaluated also the cell cycle distributions by flow cytometry (new Figure supplement 4F). These analyses show that the expression of a phospho-mimicking GTSE1 mutant induces a decrease in the percentage of cells in G1 and an increase in the percentage of cells in S, similarly to what observed in AMBRA1 KO cells.
Reviewer #3 (public review)
Summary:
This paper identifies GTSE1 as a potential substrate of cyclin D1-CDK4/6 and shows that GTSE1 correlates with cancer prognosis, probably through an effect on cell proliferation. The main problem is that the phosphorylation analysis relies on the over-expression of cyclin D1. It is unclear if the endogenous cyclin D1 is responsible for any phosphorylation of GTSE1 in vivo, and what, if anything, this moderate amount of GTSE1 phosphorylation does to drive proliferation.
Strengths:
There are few bonafide cyclin D1-Cdk4/6 substrates identified to be important in vivo so GTSE1 represents a potentially important finding for the field. Currently, the only cyclin D1 substrates involved in proliferation are the Rb family proteins.
Weaknesses:
The main weakness is that it is unclear if the endogenous cyclin D1 is responsible for phosphorylating GTSE1 in the G1 phase. For example, in Figure 2G there doesn't seem to be a higher band in the phos-tag gel in the early time points for the parental cells. This experiment could be redone with the addition of palbociclib to the parental to see if there is a reduction in GTSE1 phosphorylation and an increase in the amount in the G1 phase as predicted by the authors' model. The experiments involving palbociclib do not disentangle cell cycle effects. Adding Cdk4 inhibitors will progressively arrest more and more cells in the G1 phase and so there will be a reduction not just in Cdk4 activity but also in Cdk2 and Cdk1 activity. More experiments, like the serum starvation/release in Figure 2G, with synchronized populations of cells would be needed to disentangle the cell cycle effects of palbociclib treatment.
Please see last paragraph in the response to Reviewer #1. Concerning the experiments involving palbociclib, we limited confounding effects on the cell cycle by treating cells with palbociclib for only 4-6 hours. Under these conditions, there is simply not enough time for S and G2 cells to arrest in G1.
It is unclear if GTSE1 drives the G1/S transition. Presumably, this is part of the authors' model and should be tested.
We are not claiming that GTSE1 drives the G1/S transition (please see last paragraph in the response to Reviewer #1). GTSE1 is known to promote cell proliferation, but how it performs this task is not well understood. Our experiments indicate that, when overexpressed, cyclin D1 promotes GTSE1 phosphorylation and its consequent stabilization. In agreement with the literature, we show that higher levels of GTSE1 promote cell proliferation. To measure cell cycle distribution upon expressing various forms of GTSE1, we have now performed FACS analyses (new Figure supplement 4F). These analyses show that the expression of a phospho-mimicking GTSE1 mutant induces a decrease in the percentage of cells in G1 and an increase in the percentage of cells in S, similarly to what observed in AMBRA1 KO cells shown in the same panel and in Simoneschi et al. (Nature 2021, PMC8875297).
The proliferation assays need to be more quantitative. Figure 4B should be plotted on a log scale so that the slope can be used to infer the proliferation rate of an exponentially increasing population of cells. Figure 4c should be done with more replicates and error analysis since the effects shown in the lower right-hand panel are modest.
In Figure 4B, we plotted data in a linear scale as done in the past (Donato et al. Nature Cell Biol. 2017, PMC5376241) to better underline the changes in total cell number overtime. The experiments in Figure 4B were performed in triplicate, statistical significance was determined using unpaired T-tests with p-values<0.05, and error bars represent the mean +/- SEM. In Figure 4C, error analysis was not included for simplicity, given the complexity of the data. We have now included the other two sets of experiments (new Figure supplement 4D,E). While the effects shown in the lower right-hand panel of Figure 4C are modest, they demonstrate the same trend as those observed in the AMBRA KO cells (Figure 4C and Simoneschi et al., Nature 2021, PMC8875297). It's important to note that this effect is achieved through the stable expression of a single phospho-mimicking protein, whereas AMBRA KO cells exhibit changes in numerous cell cycle regulators. Moreover, these effects are obtained by growing cells in culture for only 5 days. A similar impact on cell growth in vivo over an extended period could pose significant risks in the long term.
Recommendations for the authors:
Reviewer #1 (Recommendations for the authors):
Figure 1E is referenced before 1D. The authors should consider switching D and E.
Done.
Figure 1D-E: The authors correctly note in the introduction that GTSE1 is encoded by a cell cycle-dependently expressed gene. Given that cell cycle genes are often associated with poor prognosis (e.g., see Whitfield et al., 2006 Nat. Rev. Cancer), this would be expected to correlate with poor prognosis. This should be mentioned in the results section.
We agree that the overexpression of certain (but not all) cell cycle-regulated genes are prognostically unfavorable across various cancer types, and we cited Whitfield et al., 2006 Nat. Rev. Cancer. However, our data indicate that phosphorylation of GTSE1 induces its stabilization and, consequently, its levels do not oscillate during the cell cycle any longer (new Figure 2G and Figure supplement 3B). Moreover, analyzing data from the Clinical Proteomic Tumor Analysis Consortium, we observed an enrichment of GTSE1 phospho-peptides (normalized to total protein) within a pan-cancer cohort as opposed to adjacent, corresponding normal tissues (Figure 2I).
Figure 2F: Contrast is too high. Blot images should not contain fully saturated black or white.
We corrected the contrast.
Figure 2G and Figure Supplement 3B: It looks like AMBRA1 KO cells do not synchronize properly in response to serum withdrawal. The cell cycle distribution should be checked by FACS. Otherwise, it is unclear whether changes in GTSE1 (phosphor) levels are only due to indirect changes in the cell cycle distribution.
Synchronization of both parental and AMBRA1 KO cells is demonstrated by the fact that the phosphorylation of Histone H3 peaks at 32 hours after serum readdition in both cases (Figure supplement 3B).
Figure 2I: It is important that phosphor-GTSE1 levels are normalized to total GTSE1 levels to understand the distinct contribution of changes in GTSE1 levels and from CCND1-CDK4 driven phosphorylation.
Done.
Figure 3A-B: These experiments should also be controlled for cell cycle distribution. Is this effect specific to GTSE1 and other AMBRA1 targets or are other G2/M cell cycle proteins also affected?
The relative short half-life of GTSE1 (<4 hours) makes its levels sensitive to acute treatments such as Palbociclib or acute AMBRA1 depletion. The effects of these treatments on GTSE1 levels are measurable within a time frame too short to significantly affect cell cycle progression. For example, we used cells with fusion of endogenous AMBRA1 to a mini-Auxin Inducible Degron (mAID) at the N-terminus. This system allows for rapid and inducible degradation of AMBRA1 upon addition of auxin, thereby minimizing compensatory cellular rewiring. Again, we observed an increase in GTSE1 levels upon acute ablation of AMBRA1 (i.e., in 8 hours) (Figure 3B), when no significant effects on cell cycle distribution are observed (please see Simoneschi et al., Nature 2021, PMC8875297 and Rona et al., Mol. Cell 2024, PMC10997477).
Figure 4: It should be noted that the correlation with cell proliferation and cell cycle protein expression is expected for any cell cycle protein, including GTSE1.
Actually, the main point of Figure 4 is to show that expression of the phospho-mimicking mutant of GTSE1 promotes cell proliferation. Comparative analysis revealed that cells overexpressing either wild-type GTSE1 or its phospho-deficient form exhibited significantly reduced proliferation rates compared to those expressing the phospho-mimicking mutant (Figure 4B,C).
The two-decades-old references 33 and 34 are not well suited to support the notion for Cyclin D1 that "the full spectrum of substrates and their impact on cellular function and oncogenesis remain poorly explored." More recent references should be used to show that this is still the case.
We added more recent references.
The authors conclude that their "data indicate that cyclin D1-CDK4 is responsible for the phosphorylation of GTSE1 on four residues (S91, S262, S454, and S724)." However, the authors' data do not exclude a role for their siblings cyclin D2, cyclin D3, and CDK6. Reflecting this, the conclusions should be toned down.
The analysis of the sites phosphorylated in GTSE1 was performed by experimentally co-expressing cyclin D1-CDK4 (Figure 2F, Figure 2H, and Figure supplement 3A), hence our statement. Yet, we agree that in cells, cyclin D2, cyclin D3, and CDK6 can contribute to GTSE1 phosphorylation.
The authors claim that they "observed that in human cells, when D-type cyclins are stabilized in the absence of AMBRA1, GTSE1 becomes phosphorylated also in G1." However, the G1-specific data presented by the authors are not controlled for, and it is unclear whether these phosphorylation events actually occur in G1 cells.
We now provide a WB in which GTSE1 phosphorylation is more evident (top panel of the new Figure 2G) (please see point (ii) in the response to the public review of Reviewer #1). This experiment clearly shows that in AMBRA1 KO cells, GTSE1 is phosphorylated at all points in the cell cycle. Synchronization of both parental and AMBRA1 KO cells is demonstrated by the fact that phosphorylation of Histone H3 peaks at 32 hours after serum re-addition in both cases (Figure supplement 3B).
Reviewer #2 (Recommendations for the authors):
(1) It is not clear from the presented data at which point in the cell cycle that phosphorylation of GTSE1 may be affecting the steady state level of the protein. The implication that GTSE1 is a target of CycD-CDK4 would suggest that the protein is stabilized at G1/S. Can this effect be observed?
Please see the last paragraph in the response to the public review of Reviewer #1.
(2) Considering the previous study showing that GTSE1 is also phosphorylated during mitosis by CycB-Cdk1, do levels of GTSE1 protein change during the cell cycle? Do changes in GTSE1 levels correlate with phosphorylation during the cell cycle? Cell synchronization experiments such as double thymidine and subsequent phostag analysis could shed some light on these questions.
Please see the last paragraph in the response to the public review of Reviewer #1.
(3) The authors show that the phosphomimetic mutants of GTSE1 confer a growth advantage on cells. The mechanism of this growth advantage is unclear. Is this effect due to a shorter cell cycle, enhanced survival, or another mechanism?
We did not observe increased cell survival when the phosphomimetic mutants of GTSE1 is expressed. We show that phosphorylation of GTSE1 induces its stabilization, leading to increased levels that, as expected based on the existing literature, contribute to enhanced cell proliferation. So, the role of the cyclin D1-CDK4/6 kinase-dependent phosphorylation of GTSE1 is to stabilize GTSE1.
(4) Other minor points - all of the presented immunoblots do not show molecular weight markers. The IF images require scale bars.
To prevent overcrowding of the Figures, the sizes of blotted proteins are indicated in the uncropped scans of each blot. Uncropped scans have been deposited in Mendeley at: https://data.mendeley.com/datasets/xzkw7hrwjr/1. Scale bars have been added to the IF images.
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Author response:
The following is the authors’ response to the original reviews.
Public Reviews:
Reviewer #1 (Public review):
Gray and colleagues describe the identification of Integrator complex subunit 12 (INTS12) as a contributor to HIV latency in two different cell lines and in cells isolated from the blood of people living with HIV. The authors employed a high-throughput CRISPR screening strategy to knock down genes and assess their relevance in maintaining HIV latency. They had used a similar approach in two previous studies, finding genes required for latency reactivation or genes preventing it and whose knockdown could enhance the latency-reactivating effect of the NFκB activator AZD5582. This work builds on the latter approach by testing the ability of gene knockdowns to complement the latency-reactivating effects of AZD5582 in combination with the BET inhibitor I-BET151. This drug combination was selected because it has been previously shown to display synergistic effects on latency reactivation.
The finding that INTS12 may play a role in HIV latency is novel, and the effect of its knockdown in inducing HIV transcription in primary cells, albeit in only a subset of donors, is intriguing. However, there are some data and clarifications that would be important to include to complement the information provided in the current version of the manuscript.
We have now added the requested data and clarifications. In particular, we show that knockout of INTS12 has no effect on cell proliferation (new data added in Figure 2—figure supplement 3)), we clarify how the degree of knockout and the complementation were accomplished, we clarify the differences between the RNA-seq and the activation scores, and we have bolstered the claim that INTS12 affected transcription elongation by performing CUT&Tag on Ser2 phosphorylation of the C-terminal tail of RNAPII along the length of the provirus (new data added in Figure 5C) Please see detailed responses below.
Reviewer #2 (Public review):
Summary:
Identifying an important role for the Integrator complex in repressing HIV transcription and suggesting that by targeting subunits of this complex specifically, INTS12, reversal of latency with and without latency reversal agents can be enhanced.
Strengths:
The strengths of the paper include the general strategy for screening targets that may activate HIV latency and the rigor of exploring the mechanism of INTS12 repression of HIV transcriptional elongation. I found the mechanism of INTS12 interesting and maybe even the most impactful part of the findings.
Weaknesses:
I have two minor comments:
There was an opportunity to examine a larger panel of latency reversal agents that reactivate by different mechanisms to determine whether INTS12 and transcriptional elongation are limiting for a broad spectrum of latency reversal agents.
I felt the authors could have extended their discussion of how exquisitely sensitive HIV transcription is to pausing and transcriptional elongation and the insights this provides about general HIV transcriptional regulation.
We have now added data on latency reversal agents of different mechanisms of action. We show that INTS12 affects HIV latency reversal from agents that affect the non-canonical NF-kB pathway (AZD5582), the canonical NF-kB pathway (TNF-alpha), activation via the T-cell receptor (CD3/CD28 antibodies), through bromodomain inhibition (I-BET151), and through a histone deacetylase inhibitor (SAHA). This additional data has been added to the manuscript in Figure 7, panels B and C as well as adding text to the discussion.
We appreciate the suggestion to extend the discussion to emphasize how important pausing and elongation are to HIV transcription. Additionally, to further support our claim that INTS12KO with AZD5582 & I-BET151 leads to an increase in elongation, that we previously showed with CUT&Tag data showing an increase in total RNAPII seen in within HIV (Figure 5B), we measured RNAPII Ser2 phosphorylation (Figure 5C) and RNAPII Ser5 phosphorylation (Figure 5—figure supplement 2) and added these findings to the manuscript. Upon measuring Ser2 phosphorylation, a marker associated with elongation, we observed evidence of elongation-competent RNAPII in our AZD5582 & I-BET151 condition as well as our INTS12 KO with AZD5582 & I-BET151 condition, as we saw an increase of Ser2 phosphorylation within HIV. Despite seeing elongation-competent RNAPII in both conditions, we only saw a dramatic increase in total RNAPII for our INTS12 KO and AZD5582 & I-BET151 condition (Figure 5B), which supports that there are more elongation events and that an elongation block is overcome specifically with INTS12 KO paired with AZD5582 & I-BET151. This claim is further supported by our data showing an increase in virus in the supernatant only with the INTS12 KO with AZD5582 & I-BET151 condition in cells from PLWH (Figure 6C). We did not observe any statistically significant differences between RNAPII Ser5 phosphorylation, which might be expected as this mark is not associated with elongation (Figure 5—figure supplement 2).
Reviewer #3 (Public review):
Summary:
Transcriptionally silent HIV-1 genomes integrated into the host`s genome represent the main obstacle to an HIV-1 cure. Therefore, agents aimed at promoting HIV transcription, the so-called latency reactivating agents (LRAs) might represent useful tools to render these hidden proviruses visible to the immune system. The authors successfully identified, through multiple techniques, INTS12, a component of the Integrator complex involved in 3' processing of small nuclear RNAs U1 and U2, as a factor promoting HIV-1 latency and hindering elongation of the HIV RNA transcripts. This factor synergizes with a previously identified combination of LRAs, one of which, AZD5582, has been validated in the macaque model for HIV persistence during therapy (https://pubmed.ncbi.nlm.nih.gov/37783968/). The other compound, I-BET151, is known to synergize with AZD5582, and is a inhibitor of BET, factors counteracting the elongation of RNA transcripts.
Strengths:
The findings were confirmed through multiple screens and multiple techniques. The authors successfully mapped the identified HIV silencing factor at the HIV promoter.
Weaknesses:
(1) Initial bias:
In the choice of the genes comprised in the library, the authors readdress their previous paper (Hsieh et al.) where it is stated: "To specifically investigate host epigenetic regulators involved in the maintenance of HIV-1 latency, we generated a custom human epigenome specific sgRNA CRISPR library (HuEpi). This library contains sgRNAs targeting epigenome factors such as histones, histone binders (e.g., histone readers and chaperones), histone modifiers (e.g., histone writers and erasers), and general chromatin associated factors (e.g., RNA and DNA modifiers) (Fig 1B and 1C)".
From these figure panels, it clearly appears that the genes chosen are all belonging to the indicated pathways. While I have nothing to object to on the pertinence to HIV latency of the pathways selected, the authors should spend some words on the criteria followed to select these pathways. Other pathways involving epigenetic modifications and containing genes not represented in the indicated pathways may have been left apart.
(2) Dereplication:
From Figure 1 it appears that INTS12 alone reactivates HIV -1 from latency alone without any drug intervention as shown by the MACGeCk score of DMSO-alone controls. If INTS12 knockdown alone shows antilatency effects, why, then were they unable to identify it in their previous article (Hsieh et al., 2023)? The authors should include some words on the comparison of the results using DMSO alone with those of the previous screen that they conducted.
(3) Translational potential:
In order to propose a protein as a drug target, it is necessary to adhere to the "primum non nocere" principle in medicine. It is therefore fundamental to show the effects of INTS12 knockdown on cell viability/proliferation (and, advisably, T-cell activation). These data are not reported in the manuscript in its current form, and the authors are strongly encouraged to provide them.
Finally, as many readers may not be very familiar with the general principles behind CRISPR Cas9 screening techniques, I suggest addressing them in this excellent review: https://pmc.ncbi.nlm.nih.gov/articles/PMC7479249/.
(1) The CRISPR library used was more completely described in a previous publication (Hsieh et al, PLOS Pathogens, 2023). However, we now more explicitly refer the reader to information about the pathways targeted in the library. We also point out how initial hits in the library lead to finding genes outside of the starting library as in the follow-up screen in Figure 7 where each of the members of the INT complex are interrogated even though only INTS12 was the only member in the initial library.
(2) We understand the confusion between the hits in this paper and a previous publication. Indeed, INTS12 was observed in Hsieh et al., PLOS Pathogens, 2023 as a hit in the Venn diagram of Figure 3B of that paper, and in Figure 5A, right panel of that paper. However, it was not followed up on in the previous paper since that paper focused on a hit that was unique to increasing the potency of one particular LRA. We added text to the present manuscript to make it clear that the screens identified many of the same hits. We have also added additional data here on hit validation to underscore the reliability of the CRISPR screen. In one of the cell lines (5A8), EZH2 was a strong hit (Figure 1B). We have now added data that shows that an inhibitor to EZH2 augments the latency reversal of AZD5582/I-BET151 as predicted from the screen. This data has been added to Figure 1, figure supplement 1.
(3) We appreciate the concern that for INTS12 to be a drug target, it should not be essential to cell viability. We now show that knockout of INTS12 has no effect on cell proliferation (new data added in Figure 2—figure supplement 3). In addition, the discussion now adds additional literature references that describe how knockout of INTS12 has relatively minor effects on cell functions in comparison to knockout of other INT members which supports that the proposal that modulation of INTS12 may be more specific than targeting the catalytic modules of Integrator. Nonetheless, we completely agree with the reviewer that many other aspects of how INTS12 affects T cell functions have not been addressed as well as other potential detrimental effect of INTS12 as a drug target in vivo. We now more explicitly describe these caveats in the discussion but feel that the present manuscript is a first step with a long path ahead before the translational potential might be realized.
(4) We now cite the review of CRISPR screens suggested by the reviewer.
Responses to recommendations for the authors:
Reviewer #1 (Recommendations for the authors):
(1) The authors report in the legend of Figure 2 (and similarly in other figures) that there was "a calculated INTS12 knockout score of 76% (for the one guide used) and 69% (for one of three guides used), respectively." However, it would be helpful to show representative data on the efficiency of INTS12 knockdown in cell lines and primary cells, as well as data on the efficiency of the complementation (Figure 2C).
The knockout scores cited are the genetic assays for the efficiency based on sequence files. As the knockouts are done with multiple guides the knockout for each guide is an underestimate of the total knockout. The complementation, however, was done by adding back INTS12 in a lentiviral vector that also contains a drug resistance marker (puromycin). Cells were then selected for puromycin resistance, and therefore, all of them contain the complemented gene. What one would ideally like is a Western blot to quantify the amount of INTS12 remaining in the knockout pools. Unfortunately, despite obtaining multiple different commercial sources of INTS12 antibodies, we were unable to identify one that was suitable for Western blotting (as opposed to two that did work for CUT&Tag). Nonetheless, the functional data in primary T cells from PLWH and in J-Lat cells lines does show the even if the knockout is suboptimal, we find activation after INTS12 knockout (e.g., Figure 6).
(2) Flow cytometry methods are not reported, but was a viability dye included when testing GFP reactivation (Figure S2)? More broadly, showing data on the viability of cells post-knockdown and drug treatments would help, as cell mortality is inherently associated with latency reactivation in J-Lat cells. For the same reason, reporting viability data would be important for primary cells, as the electroporation procedure can lead to significant mortality.
We did not include viability dyes in the data for GFP activation. However, as described in the public response, we have done growth curves in J-Lat 10.6 cells with and without INTS12 knockout and find no effects on cell proliferation (Figure 2—figure supplement 3). As the reviewer points out, it is not possible to do these experiments in primary cells since the electroporation itself causes a degree of cell death. Nonetheless, we do see effects on HIV activation in these primary cells (Figure 6).
(3) Figure S2 shows a relatively high baseline expression (approximately 15%) of HIV-GFP, which is not unusual for the J-Lat 10.6 clone. However, Figure 3 appears to show no HIV RNA reads in the control condition of this same cell clone. How do the authors reconcile this discrepancy?
We believe that the discrepancies in the flow cytometry versus RNA-seq assays are due to differences in the sensitivity of the assays, the linear range of the assays especially at the lower end, and the different half-lives of RNA versus protein. We now clarify that Figure 3 does not show “no” HIV RNA at baseline, but rather values of ~30 copies per million read counts. This increases to ~800 copies per million read counts when INTS12 knockout cells are treated with AZD5582/I-BET151. These values have the same fold change predicted in Figure 4, and more closely resemble the trend in Figure 2—figure supplement 1.
(4) The combination of AZD5582 and I-BET151 consistently reactivates HIV latency (including GFP protein expression), as previously reported and as shown here by the authors. However, in Figure 5B, RPB3/RNAPII occupancy in the DMSO control appears higher than in the AAVS1KO + AZD5582 and I-BET151 samples. This should be discussed, as it could raise concerns about the robustness of RPB3/RNAPII occupancy results as a proxy for provirus elongation.
As addressed in the public comments, in order to strengthen our claims about transcriptional elongation control, we measured RNAPII Ser2 and Ser5 phosphorylation levels. We see evidence of elongation with Ser2 in the condition of concern (AAVS1 KO + AZD5582 & I-BET151) as well as our main condition of interest (INTS12 KO + AZD5582 & I-BET151) and no change in Ser5 for any condition. With both the Ser2 phosphorylation and total RNAPII as well as our virus release and transcription data we believe that we are seeing evidence of increased elongation with INTS12 KO with AZD5582 & I-BET151. One potential nuance that may not be gathered from the CUT&Tag data is the turnover rate of the polymerase. Despite the levels of RNAPII appearing lower in the condition of concern (AAVS1 KO + AZD5582 & I-BET151) compared to DMSO it is possible that low levels of elongation are occurring but that in our INTS12 KO + AZD5582 & I-BET151 condition there is more rapid elongation and this is why we can observe more RNAPII within HIV. This new data is added in Figure 5C and Figure 5—supplement 2 and its implications are now described in more detail in the discussion.
(5) The authors write that "Degree of reactivation was correlated with reservoir size as donors PH504 (star symbol) and PH543 (upside down triangle) have the largest HIV reservoirs (supplemental Figure S2)." I could not find mention of the reservoir size of these donors in the figure provided.
This confusion was caused by mislabeling of the supplement number, which we fixed, and we added additional labeling to make finding the reservoir size even more clear as this is an important part of the manuscript. This is now found in Supplemental file S4.
Reviewer #3 (Recommendations for the authors):
(1) The MAGeCK gene score is a feature that is essential for the interpretation of the results in Figure 1. The authors do quote the Li et al. paper where this score was described for the first time (https://genomebiology.biomedcentral.com/articles/10.1186/s13059-014-0554-4), however, they may understand that not all readers may be familiar with this score. Therefore a didactic short description of this score should be done when introducing the results in Figure 1.
We have added a short description to the paper to address this.
(2) Figure 4. The authors write: "Among the host genes most prominently affected by INTS12 knockout with AZD5582 & I-BET151 are MAFA, MAFB, and ID2 (full list of genes in supplemental file S3)." I am a bit confused. In the linked Excel file there is only a list of a few genes. The differentially expressed genes appear to be many more from Figure 4. The full list should be uploaded.
We believe there was a mistake in our original uploading and naming of the supplements. We have now double-checked numbering on the supplements and added in text clarification of which excel tabs hold the desired information.
(3) Figure 6: The authors are right in highlighting that there is a high level of variability in viral RNA in supernatants in the early stages of viral reactivation. It is therefore advisable to repeat measurements at Day 7, at which variability decreases and data are more reliable (please, see: https://www.thelancet.com/journals/ebiom/article/PIIS2352-3964(23)00443-7/fulltext).
While it would have been nice to prolong these measurements, our current assay conditions are not optimal for longer term growth of the cells. We note that the measurements were all done in biological triplicates (independent knockouts) and in different individuals. Because the number of activatable latent proviruses is variable and the number of cells tested is limiting, the variability in the assays is expected.
(4) Figure 7: The main genes outside the INTS family should be identified, also.
We include the full list in supplemental file S5 and sort by most enriched.
(5) Methods: A statistical paragraph should be added in the Methods section, detailing the data analysis procedures and the key parameters utilized (for example, which is the MAGeCK gene score threshold that they used to consider knockdown efficacy on HIV latency?).
There is no MAGeCK score threshold that we use to determine efficacy on HIV latency. In a previous publication using CRISPR screens for HIV Dependency Factors (Montoya et al, mBio 2023), we showed that there is a relationship between the MAGeCK and the effect of that gene knockout on HIV replication (Figure 5 that paper). However, it is a continuum rather than a strict threshold and we believe that the effects on HIV latency would respond similarly. In the current paper, we have focused on the top hits rather than a comprehensive analysis of all the entire list. In case the reviewer is referring to the average and standard deviation of the non-targeting controls, we have added this to the figure legend and methods.
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
This study by Zimyanin et al. examines the role of the C. elegans chromokinesin KLP-19 in the formation and architecture of the anaphase central spindle in C. elegans zygotes. Through a combination of electron and light microscopy, along with RNAi-mediated perturbations, the authors propose that KLP-19 influences central spindle stiffness by regulating microtubule dynamics.
In Figure 5, the effect of KLP-19 depletion on central spindle microtubules appears unconvincing. The FRAP results show no significant difference with or without KLP-19, and overall microtubule density does not consistently respond to its depletion. Additionally, the double klp-19; gpr-1/2 (RNAi) condition does not exhibit a strong increase in microtubule density, though a statistical test is missing for this condition. Furthermore, the spd-1; gpr-1/2 double depletion produces a similar increase in microtubule density to most klp-19 depletion conditions, suggesting that the effect cannot be solely attributed to the absence of KLP-19.
Figure 5A shows that depletion of KLP-19 leads to an increase in tubulin signal in the spindle midzone. The reviewer is correct, that there are differences in the microtubule density between KLP-19 depletion alone and KLP-19 + GPR-1/2 depletion. While depletion of KLP-19 alone leads to a significant increase, co-depletion of GPR-1/2 and KLP-19 leads to a slight, but not significant increase. Along this line, we have added Supplementary Table 1 that contains all p-Values for the different conditions for Figure 5A. However, depletion of GPR-1/2 alone does not affect the microtubule density in the midzone, arguing that changes in pulling forces do not affect the microtubule density in the midzone. It is possible, that the double RNAi leads to a decrease in efficiency and thus a reduced effect on microtubule intensity. We will demonstrate the RNAi efficiency by western blot. Another possibility is that there are some feedback mechanisms that responds to presence/ absence of pulling forces and some of our data (not from this manuscript) hints in this direction, but we have not yet worked out the details of this. We are planning to publish this in a follow up publication.
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In response to the spd-1 + gpr-1/2 (RNAi), the reviewer is correct, that the microtubule density in the midzone is not significantly different from klp-19 (RNAi) conditions and we think it is interesting to note that spd-1 + gpr-1/2 (RNAi) leads to an increased microtubule density in the midzone. This could be, as above mentioned caused by some feedback mechanisms that responds to pulling forces, or also due to some functions of SPD-1 that affects microtubules in the midzone. Interestingly, our data also shows that metaphase spindles are significantly shorter in the absence of SPD-1 in comparison to spindles in control embryos, suggesting that SPD-1 plays a role in regulating microtubules or force transmission. We are currently working on understanding SPD-1's role in this process.
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We also agree that there is no significant effect on the microtubule turn-over as shown in Figure 5B and we have stated this in the text. Our data does show a trend to a decreased turn-over, but the difference is not significant. This could be due to the low sample number.
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Overall, we think our data, the light microscopy and even more so the EM data does show a clear effect on midzone microtubules.
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The use of hcp-6 depletion to argue that KLP-19 depletion affects central spindle elongation independently of stretched chromatin is problematic. hcp-6 encodes a component of the Condensin II complex in C. elegans, and its depletion leads to chromatin decompaction rather than the stretched, dense chromatin observed in the midzone during anaphase in klp-19 (RNAi) embryos. These conditions are not equivalent and do not effectively rule out the possibility that chromatin stretching contributes to the observed phenotype.
We agree with the reviewer that the HCP-6 experiments do not entirely rule out effects from lagging chromosomes. Proving that the reduced spindle and chromosome separation is not due to lagging chromosomes is challenging. Most of the depletions that lead to lagging chromosomes are based on defective kinetochore microtubule connections, such as depletion of KNL-1, NDC-80 or CLS-2 (CLASP). In C. elegans, this leads to the mass of Chromosomes staying behind in anaphase and increased spindle pole separation, which is not comparable to KLP-19 depletion. Perturbations that do not affect kinetochore microtubules but still lead to lagging chromosomes are often targeting cohesin or condensin. Ultimately none of these conditions are directly comparable.
A probably better way to test this would be to deplete KLP-19 only after metaphase to prevent its effect on chromosome alignment. However, this is currently not possible as the time window is about 1 minute or less. We currently do not have the tools to conduct this type of experiment. As other reviewers also criticized this experiment and its significance for the paper, we have removed this entirely and have added the following part to the discussion about the potential effect of lagging chromosomes:
" *We can not unambiguously rule out that failure to properly align chromosomes and the resulting lagging chromosomal material could also lead to some of the observed effects on spindle dynamics, such as slow chromosome segregation and pole separation rates as well as preventing spindle rupture in absence of SPD-1. However, several observations argue in favor of KLP-19 actively changing the midzone cytoskeleton network and thus affecting spindle dynamics. *
Most of the protein depletions in C. elegans that lead to lagging chromosomes are based on defective kinetochore microtubule connections, such as depletion of CeCENP-A, CeCENP-C, KNL-1 or NDC-80 (70-72). This mostly leads to the Chromosome mass staying behind in anaphase and increased spindle pole separation (70-72), which is not comparable to KLP-19 depletion. Perturbations that do not affect kinetochore microtubules but still lead to lagging chromosomes are often targeting cohesin or condensin, which depletion leads to chromatin decompaction (73-74) rather than the stretched, dense chromatin as observed in the midzone during anaphase in klp-19 (RNAi) embryos. Ultimately none of these conditions are directly comparable, making it difficult to completely rule out an effect of lagging chromosomes. A better way to test this would be to deplete KLP-19 only after metaphase to prevent its effect on chromosome alignment. However, this is currently not possible as the time window is about 1 minute or less and we do not have the tools to conduct this type of experiment.
*Based on our results we hypothesize that the observed spindle dynamics in absence of KLP-19 are not only caused by lagging chromosomes. Instead, KLP-19 RNAi results in a global rearrangement of the spindle and leads to a significant reduction of the spindle size, microtubule overlap, growth rate, and stability. Furthermore, the increase of microtubule interactions after klp-19 (RNAi) could also contribute to lagging of chromosomes and exacerbation of fragmented extrachromosomal material." *
Additionally, the authors report that KLP-19 influences astral microtubule dynamics (Figure 5E), yet in Figure 3E, they show that KLP-19 localizes exclusively to kinetochores and spindle microtubules, excluding astral microtubules and spindle poles. How do they reconcile this apparent contradiction?
We think that KLP-19 localizes also to astral Microtubules. Our KLP-19 GFP CRISPR line is very dim and this makes it hard to see. We are proposing to use a TIRF approach to image KLP-19 GFP on the C. elegans cortex, which we will include in the revised version. In addition, in support of our hypothesis of KLP-19 binding to astral Microtubules as well we would like to note that there is a PhD thesis available from Jack Martin in Josana Rodriguez Sanchez's Lab in Newcastle (LINK, will lead to a download of the thesis! ) that has reported KLP-19s localization to cortical Microtubules in C. elegans. In this thesis the author also reports an effect on astral microtubule growth.
Figure legends lack consistency and do not adhere to standard C. elegans nomenclature conventions (e.g., protein names should not be capitalized, and genetic perturbations should be italicized). Standardizing these elements would improve clarity and readability.
We have checked our figure legend and to our best knowledge the legends adhere to the C. elegans nomenclature. All RNAi conditions are lower case italicized and Protein names are capitalized as it is standard in other C. elegans publications. We have however noticed some variation in our Figures, i.e. EB-2 instead of EBP-2 and have corrected this in all figures.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Zimyanin et al, Chromokinesin Klp-19 regulates microtubule overlap and dynamics during anaphase in C. elegans.
The authors used a myriad of techniques, including confocal live-cell imaging, 2-photon microscopy, second harmonic generation imaging, FRAP, microfluidic-coupled TIRF, EM-tomography, to study spindle midzone assembly dynamics in C. elegans one-cell stage embryos. In particular, they illuminated the role of kinesin-4 KLP-19 in maintaining proper midzone length and organization. Inhibition of KLP-19 results in longer more stable midzones, implying KLP-19 functions in depolymerizing microtubules.
Indeed, much of the results in the current study are consistent with previously published results elsewhere. Nevertheless, the current work represents a tour-de-force showcase of diverse and state-of-the-art technology application to address spindle assembly dynamics. How KLP-19 functions to define microtubule length at the midzone is still not known. But the current work, with diverse and solid data, serves to highlight where future work should focus.
Minor comments:
Fig 3E / There is an unusual diagonal line bisecting the embryo. Visually this does not affect viewing of the His::GFP and KLP-19::GFP signals. However, when these signals are quantified and normalized (as in Fig 3F), the diagonal bisect displaying different background signal may impact the measurements.
We are very sorry about this line in the images. The line is due to a defect in the camera chip of the spinning disc. We will acquire new images for this Figure using our new spinning disc microscope.
Fig 4B / While the kymographs clearly show KLP-19::GFP motility on microtubules, they also show that the majority of KLP(-::GFP do not move. Perhaps some quantification and discussion of this result is appropriate?
The reviewer is correct that only a small fraction small fraction of molecules, maybe ~10%, moves. We will add this quantification to the paper and discussion. This could be due to several reasons: Many of the non-moving particles are not visibly colocalized with microtubules, which could mean they are sticking non-specifically to the surface (or sticking to small tubulin aggregates that aren't long enough to support movement). In addition, as this experiment is done in a lysate it is hard to interpret if the immobile KLP-19 is not moving because other proteins are bound along the microtubule blocking its way or if the KLP-19 requires some activation (i.e. phosphorylations) to become mobiles. We think this could be very interesting and will follow up on this in the future.
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Reviewer #2 (Significance (Required)):
Indeed, much of the results in the current study are consistent with previously published results elsewhere. Nevertheless, the current work represents a tour-de-force showcase of diverse and state-of-the-art technology application to address spindle assembly dynamics. How KLP-19 functions to define microtubule length at the midzone is still not known. But the current work, with diverse and solid data, serves to highlight where future work should focus.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
Summary:
The anaphase spindle midzone is an essential structure for cell division. It consists of antiparallel overlapping microtubules organized by the antiparallel microtubule bundler PRC1, molecular motors and other regulatory proteins. This manuscript investigates the role of KLP-19 (C. elegans ortholog of human kinesin-4 KIF4A) and SPD-1 (C. elegans ortholog of PRC1) for spindle midzone organization in the C. elegans embryo and its relevance for proper spindle function. Advanced fluorescence microscopy, 3D electron tomography, and a fluorescence microscopy-based single molecule assay in embryo lysate are used in a unique combination. The authors confirm several aspects of PRC1 and KIF4A function in anaphase, as reported in previous work, mostly in human cells and Drosophila embryos and also in C. elegans embryos. Measurements are mostly very quantitative and to a high quality standard. The main difference to previous conclusions is that here, the authors propose that KLP-19 does not interact with SPD-1, in contrast to what has been established for other animal kinesin-4s and PRC1, and instead localizes to the spindle midzone independently of PRC1 by a mechanism that remains unknown. The authors provide evidence that KLP-19 nevertheless controls microtubule overlap length as in other species and that it produces outward forces sliding midzone microtubules apart a movement that SPD-1 counteracts (presumably by friction). The manuscript presents a rich resource of carefully measured quantitative structural and dynamic C. elegans anaphase spindle data.
Major comments:
Key conclusions convincing?
(1) The key conclusions that the length of the central anaphase spindle microtubule overlap remains constant as the C.elegans spindle elongates (Fig. 1), that PRC1 indeed localizes quite precisely to these overlaps as previously assumed based on its in vitro (purified protein) behavior (Fig. 3B) and that the kinesin-4 KLP-19 controls overlap length as in other species (Fig. 3B) are all convincingly shown. What's missing are quantitative KLP-19 together with microtubule polarity profiles in the presence and absence of SPD-1, leaving it unclear to which extent this kinesin localizes to microtubule overlaps in the two situations. Such data seem crucial, given the authors' claim that KLP-19 localizes to the midzone and that this localization of KLP-19 is mostly unaffected by the absence of SPD-1.
If we understand this correctly the reviewer is asking for second harmonic imaging (SHG) together with imaging of KLP-19 GFP. This is currently not possible due to the way this imaging must be done (2-photon of GFP-Tubulin followed by the SHG). The only thing we can do is provide KLP-19 GFP profiles for control and SPD-1 depleted embryos. We can also use the line co-expressing SPD-1 Halo-tag and KLP-19 GFP to plot their respective localizations in control conditions. We are happy to provide such plots. Generally, we see KLP-19 going to the midzone in absence of SPD-1 and the SHG data does show that the overlap is increased. If KLP-19 specifically localizes to microtubule overlap (rather to i.e. microtubule ends) can currently not be distinguished in the spindle midzone. In vitro data from other labs and our in vitro assay suggests that KLP-19 does not specifically bind to antiparallel overlaps but rather microtubules in general.
(2) 'Normalized KLP-19 intensities' are used to demonstrate that the total amount of this kinesin localizing to the spindle midzone does not depend on the presence of SPD-1 (Fig. 3F). Given that this claim represents a major novelty of the study, the efficiency of the SPD-1 knock-down should be documented, ideally by western blot and fluorescence microscopy.
We agree with the reviewer and will provide western blots.
(3) The authors show convincingly that the kinesin KLP-19 contributes to outward microtubule sliding (and can contribute to spindle rupture in the absence of SPD-1) (Fig. 2), which is interesting and in line with the author's main claim.
(4) The interaction between KIF4a and PRC1 is well established in other species and has been clearly demonstrated both in cells and in vitro (with purified proteins). The authors claim that this concept does not apply to the C. elegans orthologs. To show 'in vitro' (outside of the spindle) that the C. elegans homologs KLP-19 and SPD-1 do not interact, the authors use a novel microfluidic fluorescence-based single-molecule assay in lysate (Fig. 4). Although very original, these experiments do not reach the biochemical standard of previous experiments with purified proteins without appropriate controls. Given that the lysate setup is fairly novel, it's advisable to present at least one positive control demonstrating that interactions between soluble proteins can indeed be detected using this assay. It would also be useful to show the absence of interaction between KLP-19 and SPD-1 by a more conventional method like co-IP, again with a positive control, to support the authors' claim. Eventually, experiments with purified proteins will have to unequivocally demonstrate whether KLP-19 and SPD-1 indeed do not interact - something which appears, however, to be beyond the scope of this study. Without additional experimental proof, the authors may want to indicate that these results are of more preliminary nature.
*We agree with the reviewer, and we will conduct co-IPs of SPD-1 and KLP-19. We will also add CYK-4 as a positive control as previous publications have shown the interaction of CYK-4 with SPD-1. We are now generating lines co-expressing CYK-4 GFP and SPD-1 Halo-tag for the co-IP experiments. *
(5) Unfortunately, the authors do not propose an alternative mechanism for KLP-19 localization to the midzone in SPD-1 depleted embryos, limiting the conceptual advance. Does KLP-19 bind directly to antiparallel microtubules, for example in the assay presented in Fig. 4 (where signs of microtubule crosslinking are shown for SPD-1)? If not, how would it accumulate in the midzone (if it does) in the C. elegans embryo anaphase spindle? The authors do also not propose a mechanism explaining why central antiparallel microtubule overlap length does not change as the spindle elongates in anaphase. Moreover, there is no discussion regarding the potential mechanism leading to KLP-19 controlling microtubule dynamics globally instead of locally where the motor accumulates, indicating limitations in mechanistic insight.
*We agree with the reviewer and will add these points to the discussion. *
*To address some of the points: *
*How does KLP-19 end up in the midzone? : Our data shows that localization of KLP-19 does depend on AIR-2 and BUB-1 as previously reported. However, those proteins primarily affect the formation of the midzone. The in vitro assay does not suggest that KLP-19 has a preference for overlaps, unlike SPD-1, but rather binds microtubules in general. One possible mechanism of midzone localization could be microtubule end-tagging, as has been suggested for PRC1 (SPD-1 homolog). This could lead to an accumulation of KLP-19 in the midzone. *
Why does the central overlap stay constant? : This can be explained by constant microtubule growth at the plus-ends why maintaining the overlap length. Alternatively, this could be explained by some (sophisticated) rearrangements of microtubules that ensure the overlap length stays the same. Generally, this is a very interesting question, as each of this scenario still requires that the overlap length is tightly regulated. Our data suggests that this is correlated with microtubule length in the midzone, as KLP-19 depletion leads to longer microtubules and overlap. This suggests that the regulation of microtubule dynamics might be an important factor in this process. We will add this to the discussion.
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Potential mechanism leading to KLP-19 controlling microtubule dynamics globally: We think that KLP-19 localizes to spindle and astral microtubules and regulates the dynamics on all of those, leading to a global regulation. By increasing it's concentration locally, microtubule dynamics can be regulated in the midzone. We will add data showing the localization of KLP-19 to astral microtubules.
Claims justified/preliminary and clearly presented?
The observation that the spindle length remains constant throughout anaphase in C. elegans is based on elegant, but unconventional fluorescence microscopy data (Fig. 1A & B). It would be helpful to add images of SHG and two-photon microscopy to help the reader understand the graphs. Measurements are presented based on distances between the poles. It is unclear why the distances between 15-20 µm were chosen and how they translate to anaphase progression. Can measurements be carried out across the entire duration of cell division to demonstrate that the overlap's 'constant length' property is unique to anaphase? (This could demonstrate already in Fig. 1 that the method in principle is capable of measuring different overlap lengths.)
We agree with the reviewer and have moved the SHG images from supplementary Fig. 6 to the main Figure 1A for better visibility. In addition, we have added a plot as an inset in (now) Figure 1B and C explanation of how the used spindle pole distances related to the progression through anaphase. Unfortunately, we can only acquire a single timepoint and not a live movie during the SHG.
Even though the manuscript contains an impressive amount of data, it appears to be lengthy, the motivation for several experiments is not clearly described, and the order of data presentation can probably be improved. For example, it is unclear why SPD-1 profiles are presented late and why KLP-19 profiles are missing - one would expect to see them early on as an essential characterization of the system under study. The motivation of the paragraph investigating the relation of KLP-19 and SPD-1 to HCP-6 is especially unclear (more than 1 page of text describing supplementary material).
We will go through our text again and will revise the order of presented experiments. As stated above, we have removed the HCP-6 data.
The absence of interaction between KLP-19 and SPD-1 is not demonstrated to the same quality standard as the presence of interaction between the orthologs in the literature, which should at least be mentioned.
Additional experiments essential to support the claims of the paper?
KLP-19 profiles in the presence and absence of SPD-1 seem to be essential.
We agree with the reviewer and will add this.
A co-IP of KLP-19 and SPD-1 (including positive control) to prove that the proteins are not interacting would help to support the claim.
We agree with the reviewer and will add this
Data and methods presented so that they can be reproduced? Yes.
Experiments adequately replicated and statistical analysis adequate? Yes.
Minor comments:
Generating cellular electron tomography data is very laborious. It is a pity that no raw data is provided; for example, a slice of a reconstructed tomogram or a video of whole volumes without segmentation would be an informative addition and allow assessment of the data quality.
We agree with the reviewer and will add movies of the raw electron microscopy data.
The clear evidence for direct interaction between PRC1 and kinesin-4 in other species should be correctly acknowledged throughout the text.
We agree with the reviewer and have corrected this
The average (mean or median?) values and STDs reported in the text do not appear to match those in Fig. 1D.
*We thank the reviewer for pointing this out and have corrected the figure. The violin lot showed the mean and percentiles, we have now changed the plot to show mean and STD. *
- *
The kymograph of spd-1 RNAi in Fig. 2A seems stretched, and the size based on the scale bar does not fit the values stated in the text.
We thank the reviewer for pointing this out and have corrected the figure.
The figure numbering, as stated in the text, does not seem to agree with those in Supplementary Figure 8.
*We thank the reviewer for pointing this out and have corrected the text. *
Page numbers and/or line numbers and figure numbers on the figures would help the reader to navigate the manuscript more easily.
We agree with the reviewer and have added this.
Reviewer #3 (Significance (Required)):
The manuscript is a rich resource of quantitative measurements of C.elegans' structural and dynamic spindle properties, using advanced light microscopy and 3D electron microscopy imaging. In large parts, the work confirms previous conclusions of the function of PRC1 and kinesin-4 in the anaphase spindle, but also reports some interesting differences, namely that the C.elegans proteins differ from their orthologs in that they do not interact with each other, raising the question of how the kinesin-4 KLP-19 localizes to the central spindle in this organism. This work is of interest for researchers studying cell division, and specifically spindle architecture, dynamics, and function.
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Rusia rebaja expectativas de un alto el fuego tras más de 12 horas de negociaciones con Estados UnidosWashington confirma que la situación en el mar Negro ha sido uno de los grandes asuntos en las converesaciones en RiadImagen facilitada por el ministerio de Asuntos Exteriores de Rusia de la delegación rusa saliendo del hotel Ritz-Carltonde Riad (Arabia saudí) después de las conversaciones este lunes con EE UU sobre el fin de la guerra en Ucrania.RUSSIAN FOREIGN MINISTRY PRESS SERVICE HANDOUT (EFE)Lola HierroMacarena Vidal LiyKiev / Washington - 24 MAR 2025 - 23:36 CETCompartir en WhatsappCompartir en FacebookCompartir en TwitterCompartir en BlueskyCompartir en LinkedinCopiar enlace0 Ir a los comentariosUn hermetismo casi absoluto ha rodeado la reunión entre representantes rusos y estadounidenses celebrada este lunes en Riad para negociar un posible alto el fuego en la invasión rusa de Ucrania. La cita ha concluido tras más de 12 horas y la única comunicación ofrecida a su término es que el texto de lo acordado no se publicará hasta este martes. La delegación de Kiev mantendrá nuevas conversaciones con la de Washington después de haberse visto el pasado domingo....Suscríbete 1 año por 144 18 €¡Solo esta semana!Seguir leyendoYa soy suscriptor_Antes de que los delegados se encerraran en una de las salas del Hotel Ritz-Carlton de la capital de Arabia Saudí, apenas habían trascendido detalles sobre el contenido de estas conversaciones. Washington quería arrancar a Moscú una promesa de tregua más allá de los mínimos planteados para proteger las infraestructuras críticas.El Kremlin, y esta es la novedad más reciente, buscaba resucitar el acuerdo de exportaciones de cereales en el mar Negro, una nueva prioridad que no estaba en la ecuación cuando se anunciaron estas rondas de negociaciones la semana pasada. Lo ha asegurado el portavoz del régimen ruso, Dmitri Peskov, este lunes: “El asunto de la iniciativa del mar Negro y todo lo relacionado con la renovación de la iniciativa están en la agenda de hoy”.El laconismo sobre el desarrollo de las conversaciones se extendía también a Washington. La portavoz del Departamento de Estado, Tammy Bruce, apenas ha proporcionado detalles sobre la marcha de las negociaciones en Riad, y se ha limitado a confirmar que la situación en el mar Negro ha sido uno de los grandes asuntos a abordar en el vaivén diplomático en Riad. “Estamos más cerca que nunca de lograr un alto el fuego. Estamos a un suspiro de lograrlo. Se puede conseguir: ahora estamos en el momento preciso en que necesitamos ideas frescas”, ha dicho.Mientras, Ucrania y Rusia han intercambiado ataques en otro día que ha dejado muertos y heridos. Este lunes se ha producido uno de los más graves perpetrados por Rusia en suelo ucranio, cuando un misil ha impactado en una zona residencial de la ciudad de Sumi. Hay al menos 88 heridos, de los que 17 son niños, según el Ayuntamiento. Rusia ha denunciado también la muerte de seis personas, entre ellas tres periodistas, en un ataque de artillería en Lugansk por parte de las Fuerzas Armadas ucranias. Además, en la madrugada, dos civiles murieron por un dron en la región rusa de Belgorod, según las autoridades locales.Durante la maratoniana jornada del lunes, los delegados de ambos países solo han hecho tres recesos para descansar. En el segundo de ellos, el diplomático Serguéi Karasin, al frente del equipo ruso, ha mostrado su satisfacción. “Las conversaciones se encuentran en pleno apogeo. Tiene lugar una interesante discusión de los temas más candentes”, ha dicho.Más allá del optimismo de Karasin, los únicos detalles de la cita han trascendido mediante un par de escuetas declaraciones del Kremlin que han rebajado las expectativas generadas en los últimos días acerca de una posible tregua. La portavoz del Ministerio de Asuntos Exteriores ruso, María Zajarova, ha declarado que aunque se está trabajando “en varias direcciones”, “no debe esperarse que las negociaciones produzcan un gran avance”, según Kommersant. El portavoz del presidente ruso, Vladímir Putin, ha afirmado que por ahora no planean firmar ningún documento.Mientras, Estados Unidos y Rusia siguen debatiendo sobre el futuro de Ucrania, los representantes de este país aguardan a que les vuelva a tocar el turno de entrar a la sala de reuniones con los portavoces de la Casa Blanca. Ambas delegaciones ya se reunieron el domingo también en Riad, y de esa cita, mucho más corta —apenas cuatro horas— trascendió que se abordaron cuestiones técnicas relacionadas con infraestructura y seguridad marítima. Fueron unas conversaciones “productivas y centradas”, en palabras del ministro de Defensa ucranio, Rustem Umerov, que encabeza el grupo de delegados de Kiev.Los planes de la Casa Blanca pasaban por reunirse por separado con los dos países enfrentados este lunes, y que de esos encuentros resultara algún compromiso rubricado por ambos. Lo que el representante de Donald Trump para las negociaciones más delicadas, Steve Witkoff, califica de “diplomacia de transbordo”, por la frecuencia en la que los mediadores estadounidenses van y vienen entre las partes.Ucrania, en principio, se mostró reticente, pero finalmente su delegación ha permanecido en Riad y el asesor del jefe de la oficina de Zelenski, Serhii Leshchenko, ha informado de que mantendrían un nuevo encuentro con los estadounidenses, que previsiblemente será este martes. El negociador ucranio también ha rebajado las expectativas: “Normalmente, las negociaciones no duran un día. A veces duran meses, y algunas, como los acuerdos en Oriente Próximo, duran años”, ha declarado a la agencia de noticias ucrania Unian.Leshchenko también ha asegurado que las fuerzas rusas no están atacando las instalaciones y puertos ucranios. Esta decisión del Kremlin subraya la importancia de reanudar el acuerdo sobre los cereales en el mar Negro, firmado en 2022 gracias a la mediación de Turquía y de la ONU para permitir la navegación segura para las exportaciones agrícolas ucranias. Un año después, Rusia lo rompió de manera unilateral con el argumento de que los países occidentales, socios estratégicos de Kiev, habían incumplido su compromiso de retirar las sanciones impuestas a sus exportaciones. Desde entonces, Ucrania ha mantenido abierto su corredor marítimo a golpe de bombardeo con misiles y drones contra las fuerzas navales enemigas.Estados Unidos también se ha mostrado a favor de resucitar el pacto. Si vuelve a rubricarse, Moscú podría exportar sus productos agrícolas y sus fertilizantes a través del mar Negro: a efectos prácticos, una eliminación de algunas de las sanciones económicas internacionales que han mantenido cojeando a su economía a lo largo de los tres años de guerra. Pero también interesa a Ucrania, para la que el tráfico marítimo es una línea vital para sus exportaciones, especialmente hacia Asia.Los acuerdos del mar Negro son la última de las condiciones impuestas por el Kremlin para encaminarse hacia una paz duradera con Ucrania. Pero Washington y Kiev también han presentado sus exigencias para seguir adelante. Para empezar, está el alto el fuego parcial que Trump lleva semanas intentando acordar con Zelenski y Putin. En las reuniones previas, ambos mandatarios habían accedido a una tregua para las instalaciones energéticas y otras infraestructuras críticas, pero ninguna de las dos partes ha cesado en sus ataques.Otro punto de gran interés para Estados Unidos es el control de las plantas de energía nuclear ucranias. El pasado 19 de marzo, Trump y Zelenski plantearon en una conversación telefónica que EE UU podría poseer o ayudar a administrar estas instalaciones, al menos de la Zaporiyia, la mayor de Europa, a cambio de su protección. Zelenski negó que se hubiese hablado de traspasar la propiedad, pero se mostró abierto a negociar algún tipo de acuerdo intermedio.Trump ha puesto otra condición a cambio de ofrecer protección y ayuda militar: la explotación de minerales y tierras raras ucranias. El acuerdo, cuya firma se truncó el pasado 28 de febrero, cuando Zelenski fue abroncado en público en el Despacho Oval, está a punto de cerrarse, según ha vuelto a afirmar Trump este lunes. Y el presidente estadounidense reiteraba el interés de Washington en gestionar Zaporiyia.Tu suscripción se está usando en otro dispositivo¿Quieres añadir otro usuario a tu suscripción?Añadir usuarioContinuar leyendo aquíSi continúas leyendo en este dispositivo, no se podrá leer en el otro.¿Por qué estás viendo esto?Flecha Tu suscripción se está usando en otro dispositivo y solo puedes acceder a EL PAÍS desde un dispositivo a la vez. 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predelay"),this.delay=this.isPageDataLayerDelay(),!0===this.delay?"undefined"!=typeof _dtm_dataLayerUpdate&&!0===_dtm_dataLayerUpdate?(this.sync="direct",DTM.notify("Data Layer sync completed <"+DTM.dataLayer.sync+">"),this.getUserInfo()):DTM.utils.addEvent(document,"DTMDataLayerUpdate",(function(){DTM.dataLayer.sync="event",DTM.notify("Data Layer sync completed <"+DTM.dataLayer.sync+">"),DTM.dataLayer.getUserInfo()})):(DTM.notify("Data Layer sync completed <"+DTM.dataLayer.sync+">"),this.getUserInfo()),DTM.tools.marfeel.utils.markTimeLoads("Datalayer postdelay"),setTimeout((function(){DTM.dataLayer.generated||(DTM.dataLayer.timeOutCompleted=!0,_satellite.getVar("platform")==DTM.PLATFORM.WEB&&!1===DTM.dataLayer.flags.paywallInfo&&(DTM.dataLayer.sync="timeout",DTM.dataLayer.getUserInfo(),DTM.notify("Paywall sync completed <"+DTM.dataLayer.sync+">")),DTM.dataLayer.generated=!0,DTM.notify("Data Layer "+(!0===DTM.dataLayer.asyncPV?"re":"")+"generated 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e=this.pageDataLayerParamExists("dataLayerDelay")?DTM.pageDataLayer.dataLayerDelay:"",t=this.pageDataLayerParamExists("paywallOn")?DTM.pageDataLayer.paywallOn:"";return""!=e?e:""!=t&&t},setFlag:function(e){if(void 0===this.flags[e]||!0===DTM.dataLayer.generated||!0===this.flags[e]||"timeout"==DTM.dataLayer.sync)return!1;this.flags[e]=!0;var t=!0;for(var a in this.flags)!1===this.flags[a]&&(t=!1);t&&!DTM.dataLayer.generated&&(DTM.dataLayer.generated=!0,DTM.notify("Data Layer "+(!0===DTM.dataLayer.asyncPV?"re":"")+"generated (all flags completed)"),DTM.utils.dispatchEvent("DTMDataLayerGenerated"),DTM.tools.marfeel.utils.markTimeLoads("Flags completed"))},fixes:function(){if(DTM.tools.marfeel.utils.markTimeLoads("Fixes start"),"multi ia"==_satellite.getVar("sysEnv")&&(this.setParam("page.pageInfo.sysEnv","fbia"),DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:fbia:sysEnv":"arc:fbia:sysEnv"),"portada"==_satellite.getVar("pageType")&&"home"!=_satellite.getVar("primaryCategory")&&(this.setParam("page.category.pageType","portadilla"),DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:pageType:portadillas":"arc:pageType:portadillas"),"brasil.elpais.com"==_satellite.getVar("server")&&0!=_satellite.getVar("pageName").indexOf("elpaiscom/brasil/")&&(this.setParam("page.pageInfo.pageName",_satellite.getVar("pageName").replace(/^elpaiscom\//gi,"elpaiscom/brasil/")),DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer-pageName-brasil":"arc:error-dataLayer-pageName-brasil"),_satellite.getVar("platform")==DTM.PLATFORM.FBIA&&(this.setParam("page.pageInfo.brandedContent",this.isBrandedContent(!1)),DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer-brandedcontent-ia":"arc:error-dataLayer-brandedcontent-ia"),"epmas"==_satellite.getVar("primaryCategory")){if("epmas>suscripcion>checkout"==_satellite.getVar("subCategory2")||"epmas>suscripcion>payment"==_satellite.getVar("subCategory2"))if(""!=DTM.utils.getQueryParam("wrongPayment",location.href)){var e=(-1!=_satellite.getVar("pageName").indexOf("elpaiscom/brasil")?"elpaiscom/brasil":"elpaiscom")+location.pathname+("epmas>suscripcion>checkout"==_satellite.getVar("subCategory2")?"checkout/errorpago":"payment/errorPago");this.setParam("page.pageInfo.pageName",e),this.setParam("page.category.subCategory2","epmas>suscripcion>proceso_pago_fallo"),DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer-wrongPayment":"arc:error-dataLayer-wrongPayment"}for(var t=["/suscripciones/promo-96-euros/","/suscripciones/promo-euro/","elpais.com/promo-3meses-1euro/","/promo-1-euro-dos-meses/","/promo-14-meses-96-euros/","/suscripciones/condiciones-servicios/empresas/","/suscripciones/america/digital/","/assinaturas/digital/","/assinatura/digital/","/assinatura/promo","assinaturas/condicoes","suscripciones/digital/semestral/condiciones","suscripciones/digital/bienal/condiciones","suscripciones/digital/promo","/condiciones/","assinaturas/clausula-privacidade","suscripciones/america/condiciones","suscripciones/condiciones","suscripciones/clausula","suscripciones/promo-todo","suscripciones/fin-de-semana","suscripciones/lunes-viernes","/condicoes/"],a=0,r=t.length;a<r;a++)-1!=location.pathname.indexOf(t[a])&&-1!=_satellite.getVar("pageName").indexOf("subscriptions/sign-in/")&&(this.setParam("page.pageInfo.pageName",-1!=_satellite.getVar("pageName").indexOf("elpaiscom/brasil")?"elpaiscom/brasil"+location.pathname:"elpaiscom"+location.pathname),this.setParam("page.category.subCategory2","epmas>suscripcion>productos"),DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-conditionsPage-"+t[a]:"arc:error-conditionsPage-"+t[a]);-1!=_satellite.getVar("destinationURL").indexOf("elpais.com/preguntas-frecuentes/")&&"elpaiscom/preguntas-frecuentes/"!=_satellite.getVar("pageName")&&(this.setParam("page.pageInfo.pageName","elpaiscom/preguntas-frecuentes/"),this.setParam("page.category.primaryCategory","epmas"),this.setParam("page.category.subCategory1","epmas>suscripcion"),this.setParam("page.category.subCategory2","epmas>suscripcion>preguntas-frecuentes"),this.setParam("page.category.pageType","suscripcion"),DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer-faq":"arc:error-dataLayer-faq"),-1!=_satellite.getVar("destinationURL").indexOf("elpais.com/aviso-impago")&&-1==_satellite.getVar("pageName").indexOf("aviso-impago")&&(this.setParam("page.pageInfo.pageName","elpaiscom/aviso-impago/"),this.setParam("page.category.primaryCategory","epmas"),this.setParam("page.category.subCategory1","epmas>suscripcion"),this.setParam("page.category.subCategory2","epmas>suscripcion>aviso-impago"),this.setParam("page.category.pageType","suscripcion"),DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer-avisoImpago":"arc:error-dataLayer-avisoImpago"),-1!=_satellite.getVar("destinationURL").indexOf("elpais.com/aviso-datos-de-facturacion")&&-1==_satellite.getVar("pageName").indexOf("aviso-datos-de-facturacion")&&(this.setParam("page.pageInfo.pageName","elpaiscom/aviso-datos-de-facturacion/"),this.setParam("page.category.primaryCategory","epmas"),this.setParam("page.category.subCategory1","epmas>suscripcion"),this.setParam("page.category.subCategory2","epmas>suscripcion>aviso-datos-de-facturacion"),this.setParam("page.category.pageType","suscripcion"),DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer-aviso-datos-de-facturacion":"arc:error-dataLayer-aviso-datos-de-facturacion")}-1!=_satellite.getVar("pageName").indexOf("elpaiscom/mexico")&&"mexico"!=_satellite.getVar("edition")?(this.setParam("page.pageInfo.edition","mexico"),DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer-edition":"arc:error-dataLayer-edition"):-1==_satellite.getVar("pageName").indexOf("elpaiscom/america/")&&-1==_satellite.getVar("pageName").indexOf("elpaiscom/suscripciones/america")||"america"==_satellite.getVar("edition")?-1!=_satellite.getVar("pageName").indexOf("elpaiscom/english")&&"english"!=_satellite.getVar("edition")?(this.setParam("page.pageInfo.edition","english"),DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer-edition":"arc:error-dataLayer-edition"):-1!=_satellite.getVar("pageName").indexOf("elpaiscom/brasil")&&"brasil"!=_satellite.getVar("edition")?(this.setParam("page.pageInfo.edition","brasil"),DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer-edition":"arc:error-dataLayer-edition"):-1!=_satellite.getVar("pageName").indexOf("elpaiscom/chile")&&"chile"!=_satellite.getVar("edition")?(this.setParam("page.pageInfo.edition","chile"),DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer-edition":"arc:error-dataLayer-edition"):-1!=_satellite.getVar("pageName").indexOf("elpaiscom/argentina")&&"argentina"!=_satellite.getVar("edition")?(this.setParam("page.pageInfo.edition","argentina"),DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer-edition":"arc:error-dataLayer-edition"):-1!=_satellite.getVar("pageName").indexOf("elpaiscom/america-colombia")&&"colombia"!=_satellite.getVar("edition")&&(this.setParam("page.pageInfo.edition","colombia"),DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer-edition":"arc:error-dataLayer-edition"):(this.setParam("page.pageInfo.edition","america"),DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer-edition":"arc:error-dataLayer-edition"),"1"!=_satellite.getVar("onsiteSearch")||DTM.utils.getQueryParam("q")||(this.setParam("page.pageInfo.onsiteSearch","0"),DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", buscador:onsiteSearch":"buscador:onsiteSearch"),DTM.tools.marfeel.utils.markTimeLoads("Fixes End")},pageDataLayerParamExists:function(e){return"undefined"!=typeof DTM&&void 0!==DTM.pageDataLayer&&(void 0!==DTM.pageDataLayer[e]||"string"==typeof DTM.pageDataLayer[e]&&""==DTM.pageDataLayer[e])},paramExists:function(e){if("string"==typeof e){var t=e.split("."),a=t.length,r=window.digitalData[t[0]];if(void 0===r)return!1;if(a>1){for(var i=1;i<a;i++)if(void 0===(r=r[t[i]]))return!1;return!0}return!0}return!1},setParam:function(e,t){if(!this.paramExists(e)||"string"!=typeof e||void 0===t)return!1;var a=e.split(".");switch(a.length){case 1:digitalData[a[0]]=t;break;case 2:digitalData[a[0]][a[1]]=t;break;case 3:digitalData[a[0]][a[1]][a[2]]=t;break;default:return!1}},formatDataLayerParam:function(e){return!!DTM.dataLayer.pageDataLayerParamExists(e)&&("string"!=typeof 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el referringDomain: "+e,"error")}return e},getPageHeight:function(){return this.vars.platform==DTM.PLATFORM.WEB&&void 0!==document.body&&void 0!==document.body.clientHeight?document.body.clientHeight:"not-set"},getPublisherID:function(){var e="";if(this.vars.platform==DTM.PLATFORM.WEB&&(e="ElpaisWeb","elpais.com"==this.vars.server||"cincodias.elpais.com"==this.vars.server)){var t={deportes:"ElpaisdeportesWeb","mamas-papas":"ElpaismamasypapasWeb",tecnologia:"ElpaistecnologiaWeb",icon:"ElpaisiconWeb","icon-design":"IcondesignWeb"},a=/http.?:\/\/([^\/]*)\/([^\/]*)\//i.exec(this.vars.destinationURL);e=this.vars.destinationURL.indexOf("el-comidista")>-1?"ElcomidistaelpaisWeb":this.vars.destinationURL.indexOf("cincodias")>-1?"CincodiaselpaisWeb":a&&t.hasOwnProperty(a[2])?t[a[2]]:"ElpaisWeb"}return e},getArticleID:function(){var e=this.pageDataLayerParamExists("destinationURL")?DTM.pageDataLayer.destinationURL:location.href,t=/http.?:\/\/([^\/]*)\/([^\/]*)\/(\d+)\/(\d+)\/(\d+)\/([^\/]*)\/(.*)\.html/i.exec(e);return t?t[7]:""},getArticleTitle:function(){if("articulo"!=this.vars.pageType)return"";var e=DTM.utils.getMetas("property","og:title");return""!=e?e[0]:this.vars.pageTitle},getCampaign:function(){for(var e="",t="",a=["id_externo_display","id_externo_sem","id_externo_nwl","id_externo_promo","id_externo_rsoc","id_externo_ref","id_externo_portada","id_externo_noti","sdi","sse","sma","prm","sap","ssm","afl","agr","int","noti","idexterno","cid","utm_campaign"],r=0,i=a.length;r<i;r++){var s=DTM.utils.getQueryParam(a[r]);""!=s&&(e=s,t=a[r])}if("id_externo_rsoc"==t||"ssm"==t){var n=DTM.utils.getQueryParam("id_externo_ads");e=""!=(n=""==n?DTM.utils.getQueryParam("ads"):n)?e+"-"+n:e}else if("prm"==t){var o=DTM.utils.getQueryParam("csl");e=""!=o?e+"_"+o:e}else"cid"==t&&(e=DTM.utils.encoder.decode(DTM.utils.decodeURIComponent(e)));return document.location.href.indexOf("utm_campaign")>-1&&(e=document.location.href.match(/utm\_campaign.*/gi)[0].split("&")[0].split("=")[1]),e},isBrandedContent:function(e){var t=!1;if(!1===e||!this.pageDataLayerParamExists("brandedContent")||"1"!=DTM.pageDataLayer.brandedContent&&1!=DTM.pageDataLayer.brandedContent){var a=JSON.stringify(this.vars.tags);!0!==(t=-1!=a.indexOf('"192925"')||-1!=a.indexOf('"197500"')||-1!=a.indexOf('"197760"')||-1!=a.indexOf('"branded_content'))&&(t=-1!=this.vars.secondaryCategories.indexOf("branded_content")||-1!=this.vars.secondaryCategories.indexOf("brandedContent"))}else t=!0;return!0===t?"1":"0"},getUrlParams:function(){var e=location.href;return this.vars.platform==DTM.PLATFORM.FBIA&&(e=DTM.utils.getQueryParam("destinationURL",location.href)),e=""!=e?e:location.href,DTM.utils.getQueryParam("",e)},getDeviceType:function(){var e=navigator.userAgent;return/(tablet|ipad|playbook|silk)|(android(?!.*mobi))/i.test(e)?"tablet":/Mobile|iP(hone|od)|Android|BlackBerry|IEMobile|Kindle|Silk-Accelerated|(hpw|web)OS|Opera M(obi|ini)/.test(e)?"mobile":"desktop"},getARCID:function(){var e="not-set";try{var t=DTM.utils.localStorage.getItem("ArcId.USER_INFO"),a=DTM.utils.localStorage.getItem("ArcP");null!=t?e=null!=(t=JSON.parse(t))&&t.hasOwnProperty("uuid")?t.uuid:"not-set":null!=a&&(a=JSON.parse(DTM.utils.localStorage.getItem("ArcP"))).hasOwnProperty("anonymous")&&a.anonymous.hasOwnProperty("reg")&&a.anonymous.reg.hasOwnProperty("l")&&!0===a.anonymous.reg.l&&(e=null!=t&&t.hasOwnProperty("uuid")?t.uuid:"not-set")}catch(t){DTM.notify("Error al acceder al item ArcId.USER_INFO de localStorage","error"),e="not-set"}return e},getUserInfo:function(){if(DTM.tools.marfeel.utils.markTimeLoads("getUserInfo pre execute"),null!=DTM.utils.getCookie("pmuser"))try{var e="not-set",t="",a="",r="not-set",i=DTM.utils.getCookie("eptz");t=null!=(s=JSON.parse(DTM.utils.getCookie("pmuser"))).NOM?s.NOM:"",e=null!=s.uid?s.uid:DTM.utils.getVisitorID(),a="T1"==s.UT||"T2"==s.UT?"suscriptor":"REGISTERED"==s.UT?"registrado":"anonimo","T1"==s.UT&&(r="T1"),"T2"==s.UT&&(r="T2"),DTM.dataLayer.setParam("user.registeredUser","ANONYMOUS"!=s.UT?"1":"0"),DTM.dataLayer.setParam("user.type",a),DTM.dataLayer.setParam("user.subscriptionType",r),DTM.dataLayer.setParam("user.profileID",""!=e?e:"not-set"),DTM.dataLayer.setParam("user.name",t),DTM.dataLayer.setParam("user.country",null==i?"not-set":i),DTM.dataLayer.setParam("user.experienceCloudID",DTM.utils.getVisitorID())}catch(e){console.log(e)}else if(null!=DTM.utils.getCookie("uid_ns"))try{var s;e="not-set",t="",i=DTM.utils.getCookie("eptz");t=null!=(s=DTM.utils.getCookie("uid_ns").split("#"))[s.length-3]?s[s.length-3]:"",e=null!=s[0]?s[0]:"",DTM.dataLayer.setParam("user.registeredUser",null!=s[s.length-3]?"1":"0"),DTM.dataLayer.setParam("user.type",null!=s[s.length-3]?"registrado":"anonimo"),DTM.dataLayer.setParam("user.profileID",""!=e?e:"not-set"),DTM.dataLayer.setParam("user.name",t),DTM.dataLayer.setParam("user.country",null==i?"not-set":i),DTM.dataLayer.setParam("user.experienceCloudID",DTM.utils.getVisitorID())}catch(e){console.log(e)}else 1==DTM.dataLayer.delay&&DTM.dataLayer.pageDataLayerParamExists("profileID")&&"not-set"!=DTM.pageDataLayer.profileID?(DTM.dataLayer.setParam("user.country",DTM.dataLayer.pageDataLayerParamExists("country")?DTM.pageDataLayer.country:""),DTM.dataLayer.setParam("user.profileID",DTM.dataLayer.pageDataLayerParamExists("profileID")?DTM.pageDataLayer.profileID:"not-set"),DTM.dataLayer.setParam("user.registeredUser",DTM.dataLayer.pageDataLayerParamExists("registeredUser")?"number"==typeof DTM.pageDataLayer.registeredUser?DTM.pageDataLayer.registeredUser.toString():DTM.pageDataLayer.registeredUser:"not-set"),DTM.dataLayer.setParam("user.ID",DTM.dataLayer.pageDataLayerParamExists("userID")?DTM.pageDataLayer.userID:DTM.dataLayer.getARCID()),DTM.dataLayer.setParam("user.name",DTM.dataLayer.pageDataLayerParamExists("userName")?DTM.pageDataLayer.userName:"not-set"),DTM.dataLayer.setParam("page.pageInfo.editionNavigation",DTM.dataLayer.pageDataLayerParamExists("editionNavigation")?DTM.pageDataLayer.editionNavigation:"not-set"),DTM.dataLayer.setParam("user.experienceCloudID",DTM.utils.getVisitorID()),DTM.notify("User Info received from Data Layer updated")):(DTM.notify("User info not calculated","error"),DTM.dataLayer.setParam("user.experienceCloudID",DTM.utils.getVisitorID()),DTM.dataLayer.setParam("user.profileID",DTM.utils.getVisitorID()),DTM.dataLayer.setParam("user.registeredUser","0"),DTM.dataLayer.setParam("user.type","anonimo"));DTM.dataLayer.setFlag("userInfo"),DTM.dataLayer.paywall.getPaywallInfo(),DTM.tools.marfeel.utils.markTimeLoads("getUserInfo post execute")},paywall:{cookieSusc:"pmuser",products:_satellite.getVar("paywall:productList"),cartSections:["epmas>suscripcion>home","epmas>suscripcion>checkout","epmas>suscripcion>confirmation","epmas>suscripcion>payment","epmas>suscripcion>login","epmas>suscripcion>registro","epmas>suscripcion>verify-gift","epmas>suscripcion>regalo-aniversario"],cookiePaywallProduct:!1,getPaywallInfo:function(){this.getPaywallAccess(),this.getPaywallType(),this.getUserType(),this.getUserSubscriptions(),this.getSignwallType(),this.getPaywallActive(),this.getPaywallContentAdType(),this.getPaywallCounter(),this.getPaywallContentBlocked(),this.getPaywallCartProduct(),this.getPaywallTransactionOrigin(),this.getPaywallTransactionType(),DTM.notify("Paywall info calculated"),DTM.dataLayer.setFlag("paywallInfo")},getUserType:function(){var e=DTM.dataLayer.pageDataLayerParamExists("userType")?DTM.pageDataLayer.userType:"not-set",t="not-set",a=e,r=[];if("0"==_satellite.getVar("user:registeredUser"))return DTM.dataLayer.setParam("user.type","anonimo"),void(this.cookiePaywallProduct="no-suscriptor");try{var i=DTM.utils.getCookie(this.cookieSusc);if(null!=i){var s=JSON.parse(i);r=s.skus;var n=!1;"T1"!=s.UT&&"T2"!=s.UT||(n=!0,t="suscriptor"),n||(t="1"==_satellite.getVar("user:registeredUser")?"registrado":"not-set")}}catch(e){DTM.notify("Error al calcular el userType","error"),t="not-set"}return a="not-set"!=e&&DTM.dataLayer.delay?e:t,DTM.dataLayer.setParam("user.type",a),r.length>0&&(this.cookiePaywallProduct=r.join(",")),a},getPaywallAccess:function(){"not-set"==_satellite.getVar("paywall:access")&&("brasil.elpais.com"==_satellite.getVar("server")||"english.elpais.com"==_satellite.getVar("server")?DTM.dataLayer.setParam("paywall.access",_satellite.getVar("server")):DTM.dataLayer.setParam("paywall.access","elpais.com"))},getSignwallType:function(){DTM.dataLayer.pageDataLayerParamExists("signwallType")?DTM.dataLayer.setParam("paywall.signwallType",DTM.pageDataLayer.signwallType):DTM.dataLayer.pageDataLayerParamExists("paywallType")?DTM.dataLayer.setParam("paywall.signwallType",DTM.pageDataLayer.paywallType):DTM.dataLayer.setParam("paywall.signwallType","free"),"freemium"==_satellite.getVar("paywall:type")&&"reg_metered"==_satellite.getVar("paywall:signwallType")&&"elpais.com"!=_satellite.getVar("server")&&(DTM.dataLayer.setParam("paywall.signwallType","free"),DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer:signwallType:ediciones":"arc:error-dataLayer:signwallType:ediciones")},getPaywallActive:function(){DTM.dataLayer.pageDataLayerParamExists("paywallActive")?(DTM.dataLayer.setParam("paywall.active",DTM.pageDataLayer.paywallActive),"freemium"==_satellite.getVar("paywall:type")&&"reg_metered"==_satellite.getVar("paywall:signwallType")&&!0===DTM.pageDataLayer.paywallActive&&(DTM.dataLayer.setParam("paywall.active",!1),DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer:reg_metered:paywallActive":"arc:error-dataLayer:reg_metered:paywallActive")):0==DTM.dataLayer.delay?DTM.dataLayer.setParam("paywall.active",!1):"timeout"!=DTM.dataLayer.sync?(DTM.dataLayer.setParam("paywall.active",!1), DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer-paywallActive":"arc:error-dataLayer-paywallActive"):DTM.dataLayer.setParam("paywall.active","not-set")},getPaywallTransactionOrigin:function(){if(DTM.dataLayer.setParam("paywall.transactionOrigin",DTM.dataLayer.pageDataLayerParamExists("transactionOrigin")?DTM.pageDataLayer.transactionOrigin:""),""==_satellite.getVar("paywall:transactionOrigin")&&"epmas>suscripcion>home"==_satellite.getVar("subCategory2")||"epmas>landing_campaign_premium_user"==_satellite.getVar("subCategory2")){var e="",t=DTM.utils.decodeURIComponent(DTM.utils.getQueryParam("backURL")),a=DTM.utils.decodeURIComponent(DTM.utils.getQueryParam("adobe_mc_ref")),r=DTM.utils.decodeURIComponent(DTM.utils.getQueryParam("backURLAMP")),i=-1!=_satellite.getVar("referringURL").indexOf("elpais.com")?_satellite.getVar("referringURL"):"";if(""!=r?e=r:""!=t&&-1==e.indexOf("/subscriptions/")&&-1==e.indexOf("/suscripciones/")?e=t:""!=a?e=a:""!=i&&(e=i),-1==e.indexOf("/subscriptions/")&&-1==e.indexOf("/suscripciones/")||(e=""),""!=e)e=e.replace(/[\?#].*?$/g,""),/^((.*)elpais.com)$/.exec(e)&&(e+="/");DTM.dataLayer.setParam("paywall.transactionOrigin",e)}},getPaywallCartProduct:function(){if("not-set"==_satellite.getVar("paywall:cartProduct")&&-1!=this.cartSections.indexOf(_satellite.getVar("subCategory2"))&&"epmas>suscripcion>home"!=_satellite.getVar("subCategory2")){var e=DTM.dataLayer.pageDataLayerParamExists("paywallProduct")&&DTM.pageDataLayer.paywallProduct?DTM.pageDataLayer.paywallProduct:"not-set";if("not-set"==e){var t=DTM.utils.localStorage.getItem("sku");t&&DTM.dataLayer.setParam("paywall.cartProduct",t)}else DTM.dataLayer.setParam("paywall.cartProduct",e)}},getPaywallCounter:function(){var e=DTM.dataLayer.pageDataLayerParamExists("paywallCounter")?DTM.pageDataLayer.paywallCounter.toString():"not-set";"freemium"==_satellite.getVar("paywall:type")&&("reg_metered"!=_satellite.getVar("paywall:signwallType")&&"not-set"!=e&&(e="not-set",DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer:paywallCounter:no-reg_metered":"arc:error-dataLayer:paywallCounter:no-reg_metered"),"reg_metered"==_satellite.getVar("paywall:signwallType")&&"1"==_satellite.getVar("user:registeredUser")&&(e="usuario-logueado",DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer:paywallCounter:logueados":"arc:error-dataLayer:paywallCounter:logueados"),"reg_metered"==_satellite.getVar("paywall:signwallType")&&"signwall"==_satellite.getVar("paywall:contentAdType")&&(e="-1",DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer:paywallCounter:signwall:bloqueante":"arc:error-dataLayer:paywallCounter:signwall:bloqueante")),DTM.dataLayer.setParam("paywall.counter",e)},getPaywallContentAdType:function(){var e=DTM.dataLayer.pageDataLayerParamExists("contentAdType")?DTM.pageDataLayer.contentAdType:"",t=DTM.dataLayer.pageDataLayerParamExists("paywallAd")?DTM.pageDataLayer.paywallAd:"",a=""!=e?e:""!=t?t:(DTM.dataLayer.delay,"none");"freemium"==_satellite.getVar("paywall:type")&&"reg_metered"==_satellite.getVar("paywall:signwallType")&&"signwall"==_satellite.getVar("paywall:contentAdType")&&"1"==_satellite.getVar("user:registeredUser")&&(a="none"),DTM.dataLayer.setParam("paywall.contentAdType",a)},getPaywallContentBlocked:function(){var e=DTM.dataLayer.pageDataLayerParamExists("contentBlocked")?DTM.pageDataLayer.contentBlocked:DTM.dataLayer.pageDataLayerParamExists("paywallStatus")?DTM.pageDataLayer.paywallStatus.toString():"not-set";0==DTM.dataLayer.delay&&"free"==_satellite.getVar("paywall:signwallType")&&"0"!=_satellite.getVar("paywall:contentBlocked")?(e="0",DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer-paywallStatus":"arc:error-dataLayer-paywallStatus"):1==DTM.dataLayer.delay&&"timeout"!=DTM.dataLayer.sync&&"not-set"==e&&(e="reg"==_satellite.getVar("paywall:signwallType")&&"0"==_satellite.getVar("user:registeredUser")?"1":"0",DTM.internalTest=""!=DTM.internalTest?DTM.internalTest+", arc:error-dataLayer-contentBlocked-vacio":"arc:error-dataLayer-contentBlocked-vacio"),DTM.dataLayer.setParam("paywall.contentBlocked",e)},getUserSubscriptions:function(){var e=DTM.dataLayer.pageDataLayerParamExists("paywallProduct")&&DTM.pageDataLayer.paywallProduct?DTM.pageDataLayer.paywallProduct:"not-set",t=e,a=DTM.dataLayer.pageDataLayerParamExists("paywallProduct")&&"not-set"!=DTM.pageDataLayer.paywallProduct&&""!=DTM.pageDataLayer.paywallProduct?DTM.pageDataLayer.paywallProduct:"",r=DTM.dataLayer.pageDataLayerParamExists("paywallProductOther")&&"not-set"!=DTM.pageDataLayer.paywallProductOther&&""!=DTM.pageDataLayer.paywallProductOther?DTM.pageDataLayer.paywallProductOther:"";if("not-set"!=e&&-1==this.cartSections.indexOf(_satellite.getVar("subCategory2"))&&DTM.dataLayer.delay&&a!=r){t=""!=a&&""!=r?"brasil.elpais.com"==_satellite.getVar("server")?r+","+a:a+","+r:""!=a?e:""!=r?r:"suscriptor"==_satellite.getVar("user:type")?"not-set":"no-suscriptor"}else{t=!1!==this.cookiePaywallProduct?this.cookiePaywallProduct:"suscriptor"==_satellite.getVar("user:type")?"not-set":"no-suscriptor"}("0"==_satellite.getVar("user:registeredUser")||"registrado"==_satellite.getVar("user:type")&&"not-set"==_satellite.getVar("user:subscriptions"))&&(t="no-suscriptor"),DTM.dataLayer.setParam("user.subscriptions",t),_satellite.setVar("mboxSubscriptions",t)},getPaywallTransactionType:function(){if("epmas>suscripcion>confirmation"==_satellite.getVar("subCategory2")||"epmas>suscripcion>checkout"==_satellite.getVar("subCategory2")){var e=DTM.dataLayer.pageDataLayerParamExists("paywallTransactionType")?DTM.pageDataLayer.paywallTransactionType:"",t=DTM.dataLayer.pageDataLayerParamExists("paywallSubsType")?DTM.pageDataLayer.paywallSubsType:"",a=""!=e?e:""!=t?t:"clasico";DTM.dataLayer.setParam("paywall.transactionType",a)}},getPaywallType:function(){var e="none";DTM.dataLayer.pageDataLayerParamExists("dataLayerVersion")&&"v2"==DTM.pageDataLayer.dataLayerVersion?e="freemium":!0===DTM.dataLayer.delay&&DTM.dataLayer.pageDataLayerParamExists("videoContent")&&(e="metered"),DTM.dataLayer.setParam("paywall.type",e)}}},utils:{addEvent:function(e,t,a){document.addEventListener?e.addEventListener(t,a,!1):e.attachEvent("on"+t,a)},copyObject:function(e){if("object"!=typeof e)return!1;var t={};for(var a in e)t[a]=e[a];return t},dispatchEvent:function(e){var t;"function"==typeof Event?t=new Event(e):(t=document.createEvent("Event")).initEvent(e,!0,!0),document.dispatchEvent&&document.dispatchEvent(t)},decodeURIComponent:function(e){var t=e;try{t=decodeURIComponent(e)}catch(a){t=e,DTM.notify("decodedComponent: error al decodificar el componente: "+e,"error")}return t},encoder:{_keyStr:"ABCDEFGHIJKLMNOPQRSTUVWXYZabcdefghijklmnopqrstuvwxyz0123456789+/=",encode:function(e){var t,a,r,i,s,n,o,l="",d=0;for(e=this._utf8_encode(e);d<e.length;)i=(t=e.charCodeAt(d++))>>2,s=(3&t)<<4|(a=e.charCodeAt(d++))>>4,n=(15&a)<<2|(r=e.charCodeAt(d++))>>6,o=63&r,isNaN(a)?n=o=64:isNaN(r)&&(o=64),l=l+this._keyStr.charAt(i)+this._keyStr.charAt(s)+this._keyStr.charAt(n)+this._keyStr.charAt(o);return l},decode:function(e){var t,a,r,i,s,n,o="",l=0;for(e=e.replace(/[^A-Za-z0-9\+\/\=]/g,"");l<e.length;)t=this._keyStr.indexOf(e.charAt(l++))<<2|(i=this._keyStr.indexOf(e.charAt(l++)))>>4,a=(15&i)<<4|(s=this._keyStr.indexOf(e.charAt(l++)))>>2,r=(3&s)<<6|(n=this._keyStr.indexOf(e.charAt(l++))),o+=String.fromCharCode(t),64!=s&&(o+=String.fromCharCode(a)),64!=n&&(o+=String.fromCharCode(r));return this._utf8_decode(o)},_utf8_encode:function(e){e=e.replace(/\r\n/g,"\n");for(var t="",a=0;a<e.length;a++){var r=e.charCodeAt(a);r<128?t+=String.fromCharCode(r):r>127&&r<2048?(t+=String.fromCharCode(r>>6|192),t+=String.fromCharCode(63&r|128)):(t+=String.fromCharCode(r>>12|224),t+=String.fromCharCode(r>>6&63|128),t+=String.fromCharCode(63&r|128))}return t},_utf8_decode:function(e){for(var t="",a=0,r=c1=c2=0;a<e.length;)(r=e.charCodeAt(a))<128?(t+=String.fromCharCode(r),a++):r>191&&r<224?(c2=e.charCodeAt(a+1),t+=String.fromCharCode((31&r)<<6|63&c2),a+=2):(c2=e.charCodeAt(a+1),c3=e.charCodeAt(a+2),t+=String.fromCharCode((15&r)<<12|(63&c2)<<6|63&c3),a+=3);return t}},formatData:function(e){var t={};for(var a in e)if(null!=e[a]){if("videoName"==a)var r="object"!=typeof e[a]?e[a].toString().replace(/"/g,'\\"'):e[a];else r="object"!=typeof e[a]?e[a].toString().toLowerCase().replace(/"/g,'\\"'):e[a];switch(a){case"videoName":r=r.replace(/\-\d+$/,"").replace(/#/g,"");break;case"userID":case"pageTitle":case"videoYoutubeChannel":case"articleTitle":case"uniqueVideoID":case"photoURL":case"registerOrigin":case"registerProd":r=e[a];break;case"pageName":r=_satellite.getVar("siteID")+e[a].replace(/[\?#].*?$/g,"").replace(/http.?:\/\/[^\/]*/,"")}t[a]=r}else t[a]="";return t},formatDate:function(e){return e<10?"0"+e:e},getCookie:function(e){for(var t=e+"=",a=document.cookie.split(";"),r=0,i=a.length;r<i;r++){for(var s=a[r];" "==s.charAt(0);)s=s.substring(1,s.length);if(0==s.indexOf(t))return s.substring(t.length,s.length)}return null},checkShownBlock:function(){var e="NA",t="elpais";if(document.querySelectorAll(".b-t-ipcatalunya").length>0){var a=".b-t-ipcatalunya",r=document.querySelectorAll(".b-t-ipcatalunya > div article"),i=0;if(window.seteoVariableControl=function(){localStorage.setItem("reto_bloque_portada","reto_bloque_portada")},document.querySelector(a)&&"block"==window.getComputedStyle(document.querySelector(a)).display&&"undefined"!=typeof digitalData){for(i=0;i<r.length-1;i++)r[i].addEventListener("click",seteoVariableControl);e=e.indexOf("NA")>-1?t+":EP-R001:reto bloque portada":e+"|"+t+":EP-R001:reto bloque portada"}}document.querySelectorAll(".tooltip").length>0&&(window.seteoVariableControlTooltip=function(){localStorage.setItem("reto_tooltip","reto_tooltip")},document.querySelectorAll(".tooltip").length>0&&"undefined"!=typeof digitalData&&document.querySelector(".tooltip > article")&&(document.querySelector(".tooltip > article").addEventListener("click",seteoVariableControlTooltip),e=e.indexOf("NA")>-1?t+":tooltip":e+"|"+t+":tooltip"));return e},checkOriginBlock:function(){var e="elpais";return"reto_bloque_portada"==localStorage.getItem("reto_bloque_portada")&&"undefined"!=typeof digitalData&&document.location.href.indexOf("/espana/catalunya/")>-1?(localStorage.removeItem("reto_bloque_portada"),e+":EP-R001:reto bloque portada"):"reto_tooltip"==localStorage.getItem("reto_tooltip")&&"undefined"!=typeof digitalData?(localStorage.removeItem("reto_tooltip"),e+":tooltip"):""},checkBrowser:function(e){return e.match(/FB\_IAB|FB4A\;FBAV/i)?"Facebook":e.match(/FBAN\/EMA/i)?"Facebook Lite":e.indexOf("FB_AIB")>-1?"Facebook Messenger":e.indexOf("MessengerLite")>-1?"Facebook Messenger Lite":e.indexOf("FBAN")>-1?"Facebook Groups":e.indexOf("Instagram")>-1?"Instagram":e.indexOf("Twitter")>-1?"Twitter":e.indexOf("Twitterrific")>-1?"Twitterrific":e.indexOf("WhatsApp")>-1?"WhatsApp":e.indexOf("edge")>-1?"MS Edge":e.indexOf("edg/")>-1?"Edge (chromium based)":e.indexOf("opr")>-1&&window.opr?"Opera":e.match(/chrome|chromium|crios/i)?"Chrome":e.indexOf("trident")>-1?"IE":e.match(/firefox|fxios/i)?"Mozilla Firefox":e.match(/LinkedInApp|LinkedIn/i)?"LinkedIn":e.match(/musical\_ly|TikTokLIVEStudio/i)?"TikTok":e.indexOf("safari")>-1?"Safari":e.indexOf("Pinterest")>-1?"Pinterest":"Otros"},getMetas:function(e,t){if(!e||!t||"function"!=typeof document.getElementsByTagName)return[];e=e.toLowerCase(),t=t.toLowerCase();var a=[];if("function"==typeof document.querySelectorAll)document.querySelectorAll("meta["+e+"='"+t+"']").forEach((function(e){a.push(e.getAttribute("content"))}));else{var r=document.getElementsByTagName("meta");for(i=0,j=r.length;i<j;i++)r[i].getAttribute(e)==t&&a.push(r[i].getAttribute("content"))}return a},getQueryParam:function(e,t){var a="";if(e=void 0===e||""==e?-1:e,url=void 0===t||""==t?window.location.href:t,!1!==DTM.dataLayer.vars.urlParams&&void 0===t){var r=DTM.dataLayer.vars.urlParams;return-1!=e?r.hasOwnProperty(e)?r[e]:"":DTM.dataLayer.vars.urlParams}if(-1==e){if(a=[],-1!=url.indexOf("?"))for(var i=url.substr(url.indexOf("?")+1).replace(/\?/g,"&"),s=0,n=(i=i.split("&")).length;s<n;s++)if(-1!=i[s].indexOf("=")){var o=i[s].substr(0,i[s].indexOf("=")),l=i[s].substr(i[s].indexOf("=")+1);a[o]=l.replace(/#(.*)/g,"")}else a[i[s]]=""}else{a="",e=e.replace(/[\[]/,"\\[").replace(/[\]]/,"\\]");var d=new RegExp("[\\?&]"+e+"=([^&#]*)").exec(url);a=null==d?"":DTM.utils.decodeURIComponent(d[1].replace(/\+/g," 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i=document.getElementsByTagName("head")[0];r.addEventListener?r.addEventListener("load",(function(){t(a)}),!1):r.onload?r.onload=function(){t(a)}:document.all&&(s.onreadystatechange=function(){var e=s.readyState;"loaded"!==e&&"complete"!==e||(t(a),s.onreadystatechange=null)}),r.src=e,i.appendChild(r)},getPlayerType:function(e){var t="html5";return"string"==typeof e&&(e=e.toLowerCase()),null!=e&&(-1!=e.indexOf("youtube")?t="youtube":-1!=e.indexOf("triton")?t="triton":-1!=e.indexOf("dailymotion")?t="dailymotion":-1!=e.indexOf("jwplayer")?t="jwplayer":-1!=e.indexOf("realhls")?t="realhls":-1!=e.indexOf("html5")&&(t="html5")),t},localStorage:{getItem:function(e){var t=!1;try{"undefined"!=typeof localStorage&&"function"==typeof localStorage.getItem&&(t=localStorage.getItem(e))}catch(e){t=!1,DTM.notify("Error in getItem in localStorage","error")}return t},removeItem:function(e){var t=!1;try{"undefined"!=typeof localStorage&&"function"==typeof localStorage.removeItem&&(localStorage.removeItem(e),t=!0)}catch(e){t=!1,DTM.notify("Error in removeItem in localStorage","error")}return t},setItem:function(e,t){var a=!1;try{"undefined"!=typeof localStorage&&"function"==typeof localStorage.setItem&&(localStorage.setItem(e,t),a=!0)}catch(e){a=!1,DTM.notify("Error in setItem in localStorage","error")}return a}},parseJSON:function(e){try{return JSON.parse(e.replace(/\'/g,'"'))}catch(e){return{}}},sendBeacon:function(e,t,a,r,i){if("string"!=typeof e||"object"!=typeof t)return!1;var s=!1;try{if("undefined"==typeof navigator||"function"!=typeof navigator.sendBeacon||void 0!==a&&!0!==a){var n=new Image(1,1),o=[];for(var l in t)void 0!==i&&!1===i?o.push(l+"="+t[l]):o.push(l+"="+encodeURIComponent(t[l]));var d="";"string"==typeof r&&(d=r+"="+String(Math.random()).substr(2,9)),n.src=e.replace(/\?/gi,"")+"?"+o.join("&")+(o.length>0&&""!=d?"&":"")+d,s=!0}else s=navigator.sendBeacon(e,JSON.stringify(t))}catch(e){DTM.notify("Error in sendBeacon: "+e,"error"),s=!1}return s},setCookie:function(e,t,a,r){var i="";if(r){var s=new Date;s.setTime(s.getTime()+r),i="; expires="+s.toGMTString()}document.cookie=e+"="+t+i+";domain="+a+";path=/"},isUE:function(){try{var t=Intl.DateTimeFormat().resolvedOptions().timeZone;return!(void 0===t||!t.startsWith("Europe")&&"Atlantic/Canary"!=t)||(void 0===t||t.length<=3&&-1==t.indexOf("/"))}catch{return console.log("DTM Utils - isUE",e),!0}}},events:{ABDESACT:"ABdesact",ABDETECTED:"ABdetected",ADEND:"adEnd",ADPLAY:"adPlay",ADERROR:"adError",ADSKIP:"adSkip",ADPAUSED:"adPaused",ADRESUMED:"adResumed",ADTIMEOUT:"adTimeout",AUDIOPLAY:"audioPlay",AUDIO50:"audio50",AUDIOEND:"audioEnd",AUDIOPAUSED:"audioPaused",AUDIORESUMED:"audioResumed",AUDIOREADY:"audioReady",BUTTONCLICK:"buttonClick",USERFLOWINIT:"userFlowInit",USERFLOWEND:"userFlowEnd",NOTICEDISPLAYED:"noticeDisplayed",CHECKOUT:"checkout",COMMENTS:"comments",CONC:"conc",CONCPARTICIPATE:"concParticipate",DOWNLOADLINK:"downloadLink",EDITIONCHANGE:"editionChange",EMAILREGISTER:"emailRegister",EXITLINK:"exitLink",EXTERNALLINK:"externalLink",EXTERNALLINKART:"externalLinkArticle",FAVADD:"favAdd",FAVREMOVE:"favRemove",FORMABANDON:"formAbandon",FORMERROR:"formError",FORMSUCESS:"formSucess",GAMEPLAY:"gamePlay",GAMECOMPLETE:"gameComplete",GAMEPICKER:"gamePicker",INTERNALPIXEL:"internalPixel",INTERNALSEARCH:"internalSearch",INTERNALSEARCHEMPTY:"internalSearchEmpty",INTERNALSEARCHRESULTS:"internalSearchResults",PAGEVIEW:"pageView",PAYERROR:"payError",PAYOK:"payOK",PHOTOGALLERY:"photogallery",PHOTOZOOM:"photoZoom",POPUPIMPRESSION:"popupImpression",PRODVIEW:"prodView",PURCHASE:"purchase",READARTICLE:"readArticle",RECOMMENDERIMPRESSION:"recommenderImpression",REELPLAY:"reelPlay",REELEND:"reelEnd",SALEBUTTON:"saleButton",SCADD:"scAdd",SCCHECKOUT:"scCheckout",SCREMOVE:"scRemove",SCROLL:"scroll",SCROLLINF:"scrollInf",SCVIEW:"scView",SHARE:"share",SORT:"sort",SWIPEH:"swipeH",TEST:"test",USERCONNECT:"userConnect",USERDISCONNECT:"userDisconnect",USERLOGIN:"userLogin",USERLOGININIT:"userLoginInit",USERLOGINREGISTER:"userLoginRegister",USERLOGOFF:"userLogOFF",USERNEWSLETTERIN:"userNewsletterIN",USERNEWSLETTEROFF:"userNewsletterOFF",USERPREREGISTER:"userPreRegister",USERREGISTER:"userRegister",USERUNREGISTER:"userUnregister",USERSUBSCRIPTION:"userSubscription",USERVINC:"userVinc",UUVINC:"UUvinc",VIDEOADSERVERRESPONSE:"videoAdserverResponse",VIDEOPLAY:"videoPlay",VIDEOEND:"videoEnd",VIDEO25:"video25",VIDEO50:"video50",VIDEO75:"video75",VIDEORESUMED:"videoResumed",VIDEOPAUSED:"videoPaused",VIDEOPLAYEROK:"videoPlayerOK",VIDEOREADY:"videoReady",VIDEOSEEKINIT:"videoSeekInit",VIDEOSEEKCOMPLETE:"videoSeekComplete",VIEWARTICLE:"viewArticle",VIDEORELOAD:"videoReload",VIDEOREPLAY:"videoReplay",init:function(){function e(){var e=DTM.utils.getQueryParam("o"),t=DTM.utils.getQueryParam("prod"),a=DTM.utils.getQueryParam("event_log"),r=DTM.utils.getQueryParam("event");if("epmas>suscripcion>verify-email"==_satellite.getVar("subCategory2"))DTM.trackEvent(DTM.events.USERREGISTER,{registerType:"clasico",registerOrigin:e,registerProd:t,registerBackURL:DTM.utils.decodeURIComponent(DTM.utils.getQueryParam("backURL")),validEvent:!0});else{if(""!=r&&"1"!=_satellite.getVar("user:registeredUser"))return!1;if("okdesc"==a&&"0"!=_satellite.getVar("user:registeredUser"))return!1;if(""!=a&&"okdesc"!=a&&"1"!=_satellite.getVar("user:registeredUser"))return!1;if(""!=a){var i={oklogin:"clasico",okdesc:"clasico",okvinculacion:"clasico",fa:"facebook",tw:"twitter",go:"google",me:"msn",li:"linkedin"};if(i.hasOwnProperty(a)){var s="okdesc"==a?DTM.events.USERLOGOFF:"okvinculacion"==a?DTM.events.UUVINC:DTM.events.USERLOGIN;DTM.trackEvent(s,{registerType:i[a],registerOrigin:e,registerProd:t,validEvent:!0})}}if(""!=r){var n={okregistro:"clasico",fa:"facebook",tw:"twitter",go:"google",me:"msn",li:"linkedin"};n.hasOwnProperty(r)&&DTM.trackEvent(DTM.events.USERREGISTER,{registerType:n[r],registerOrigin:e,registerProd:t,validEvent:!0})}}DTM.notify("Event Listener added <Registers & Logins>")}if(DTM.eventQueue.length>0)for(var t=0,a=DTM.eventQueue.length;t<a;t++)DTM.eventQueue[t].hasOwnProperty("eventName")&&DTM.eventQueue[t].hasOwnProperty("data")&&(DTM.notify("Event <"+DTM.eventQueue[t].eventName+"> fired from DTM.eventQueue"),DTM.trackEvent(DTM.eventQueue[t].eventName,DTM.eventQueue[t].data));DTM.dataLayer.generated?e():DTM.utils.addEvent(document,"DTMCompleted",(function(){e()})),"articulo"==_satellite.getVar("pageType")&&(setTimeout((function(){DTM.trackEvent(DTM.events.READARTICLE)}),6e4),DTM.notify("Event Listener added <Read Article>")),"1"!=_satellite.getVar("liveContent")&&"juegos"!=_satellite.getVar("primaryCategory")||(DTM.utils.addEvent(window,"message",(function(e){try{if(void 0!==e&&void 0!==e.data)if(void 0!==e.data.eventType&&"object"==typeof e.data.data)DTM.trackEvent(e.data.eventType,e.data.data);else if("juegos"==_satellite.getVar("primaryCategory")&&-1!=e.origin.indexOf("amuselabs")&&"string"==typeof e.data&&0==e.data.indexOf("{")){var t=JSON.parse(e.data);if(t.hasOwnProperty("src")&&"crossword"==t.src&&t.hasOwnProperty("progress")){var a=t.hasOwnProperty("title")?t.title:"not-set",r=t.hasOwnProperty("id")?t.id:"not-set";"puzzleCompleted"==t.progress?DTM.trackEvent(DTM.events.GAMECOMPLETE,{gameName:a,gameID:r}):"puzzleLoaded"==t.progress&&DTM.trackEvent(DTM.events.GAMEPLAY,{gameName:a,gameID:r})}}}catch(e){DTM.notify("Error en video iframe")}}),!1),DTM.notify("Event Listener added <Video Iframes>")),function(){function e(){if(!DTM.dataLayer.generated||"escaparate"!=_satellite.getVar("primaryCategory")||"articulo"!=_satellite.getVar("pageType")||void 0===document.querySelectorAll)return!1;var e=document.querySelectorAll(".article_body a.escaparate[data-link-track-dtm]"),t=document.querySelectorAll("article .a_btn a");if(e.length>0||t.length>0)for(var a=e.length>0?e:t,r=1,i=0,s=a.length;i<s;i++){var n=a[i];if(""!=n.href&&-1==n.href.indexOf("javascript")&&-1==n.href.indexOf("//elpais.com")){n.escOrder="btn-esc-"+r++,n.escBoton=n.innerHTML.trim().toLowerCase();var o=/^(.*) en (.*)$/gi.exec(n.escBoton);n.escVendor=null!=o?o[2]:"not-set",DTM.utils.addEvent(n,"click",(function(){DTM.trackEvent(DTM.events.SALEBUTTON,{articleTitle:_satellite.getVar("pageTitle"),buttonName:this.escBoton+" ("+this.escOrder+")",externalURL:this.escVendor+":"+this.href})}))}}}"escaparate"==_satellite.getVar("primaryCategory")&&"articulo"==_satellite.getVar("pageType")&&_satellite.getVar("platform")===DTM.PLATFORM.WEB&&("complete"==document.readyState?e():DTM.utils.addEvent(window,"load",(function(){e()}),!1))}(),function(){if(""!=DTM.utils.getQueryParam("ed")){var e=DTM.utils.localStorage.getItem("dtm_changeEdition");if(null!=e){var t=(e=DTM.utils.parseJSON(e)).hasOwnProperty("editionDestination")?e.editionDestination:"not-set",a=e.hasOwnProperty("editionOrigin")?e.editionOrigin:"not-set";DTM.trackEvent("editionChange",{editionChange:a+":"+t}),DTM.utils.localStorage.removeItem("dtm_changeEdition"),DTM.notify("Event Listener added <Event Change>")}}}()},setEffect:function(e,t,a){void 0===a&&(a=!0),void 0!==e&&void 0!==t&&void 0!==window.digitalData.event[e]&&(window.digitalData.event[e].eventInfo.effect[t]=a)},validEvent:function(e){var t=!1;for(var a in this)if("string"==typeof this[a]&&this[a]==e)return!0;return t}},tools:{allowAll:!0,DISABLED:0,ENABLED:1,ONLYEVENTS:2,initialized:!1,init:function(){for(var e in DTM.tools.allowAll=void 0===DTM.config.allowAll||DTM.config.allowAll,this)"function"==typeof this[e].init&&"object"==typeof this[e].dl&&this[e].init();this.initialized=!0,DTM.notify("Tools initialized")},list:[],omniture:{enabled:1,dl:{},eventQueue:[],loaded:!1,trackedPV:!1,map:{events:{},vars:{},consents:{}},init:function(){DTM.tools.marfeel.utils.markTimeLoads("Omniture init"),this.enabled=this.isEnabled(),this.enabled!=DTM.tools.DISABLED&&DTM.tools.list.push("omniture"),this.createMap(),this.initTracker(),this.setDL({authors:this.formatListVar(_satellite.getVar("author"),"id"),cartProductPages:["epmas>suscripcion>checkout","epmas>suscripcion>payment","epmas>suscripcion>confirmation","epmas>suscripcion>verify-gift"],secondaryCategories:this.formatListVar(_satellite.getVar("secondaryCategories")),tags:this.formatListVar(_satellite.getVar("tags"),"id")})},createMap:function(){this.map.events[DTM.events.INTERNALSEARCH]="event1",this.map.events[DTM.events.PAGEVIEW]="event2",this.map.events[DTM.events.SCROLL]="event5",this.map.events[DTM.events.VIDEO25]="event8",this.map.events[DTM.events.VIDEO75]="event9",this.map.events[DTM.events.SCROLLINF]="event10",this.map.events[DTM.events.VIDEOPLAY]="event11",this.map.events[DTM.events.REELPLAY]="event48",this.map.events[DTM.events.VIDEOREPLAY]="event11",this.map.events[DTM.events.VIDEOEND]="event12",this.map.events[DTM.events.REELEND]="event49",this.map.events[DTM.events.ADPLAY]="event13",this.map.events[DTM.events.ADEND]="event14",this.map.events[DTM.events.ADSKIP]="event15",this.map.events[DTM.events.AUDIOPLAY]="event16",this.map.events[DTM.events.AUDIOEND]="event17",this.map.events[DTM.events.AUDIO50]="event18",this.map.events[DTM.events.USERPREREGISTER]="event19",this.map.events[DTM.events.USERLOGINREGISTER]="event20",this.map.events[DTM.events.USERREGISTER]="event21",this.map.events[DTM.events.EXTERNALLINK]="event22",this.map.events[DTM.events.USERLOGIN]="event23",this.map.events[DTM.events.USERLOGININIT]="event24",this.map.events[DTM.events.USERUNREGISTER]="event25",this.map.events[DTM.events.FORMABANDON]="event26",this.map.events[DTM.events.FORMSUCESS]="event27",this.map.events[DTM.events.FORMERROR]="event28",this.map.events[DTM.events.USERFLOWINIT]="event29",this.map.events[DTM.events.USERFLOWEND]="event30",this.map.events[DTM.events.BUTTONCLICK]="event33",this.map.events[DTM.events.COMMENTS]="event34",this.map.events[DTM.events.SALEBUTTON]="event35",this.map.events[DTM.events.EDITIONCHANGE]="event37",this.map.events[DTM.events.USERNEWSLETTERIN]="event38",this.map.events[DTM.events.USERNEWSLETTEROFF]="event39",this.map.events[DTM.events.SWIPEH]="event43",this.map.events[DTM.events.AUDIOPAUSED]="event44",this.map.events[DTM.events.AUDIORESUMED]="event45",this.map.events[DTM.events.CONC]="event50",this.map.events[DTM.events.GAMEPLAY]="event55",this.map.events[DTM.events.GAMECOMPLETE]="event56",this.map.events[DTM.events.GAMEPICKER]="event57",this.map.events[DTM.events.VIDEOPLAYEROK]="event59",this.map.events[DTM.events.CHECKOUT]="event60,scCheckout",this.map.events[DTM.events.PURCHASE]="event61,purchase",this.map.events[DTM.events.SHARE]="event69",this.map.events[DTM.events.PHOTOZOOM]="event76",this.map.events[DTM.events.VIEWARTICLE]="event77",this.map.events[DTM.events.PHOTOGALLERY]="event78",this.map.events[DTM.events.VIDEO50]="event79",this.map.events[DTM.events.READARTICLE]="event80",this.map.events[DTM.events.CONCPARTICIPATE]="event81",this.map.events[DTM.events.NOTICEDISPLAYED]="event89",this.map.events[DTM.events.EXTERNALLINKART]="event99",this.map.events[DTM.events.TEST]="event100",this.map.events[DTM.events.PAYOK]="event102",this.map.events[DTM.events.PAYERROR]="event103",this.map.events[DTM.events.POPUPIMPRESSION]="event113",this.map.events[DTM.events.DOWNLOADLINK]="",this.map.events[DTM.events.EXITLINK]="",this.map.vars.destinationURL="eVar1",this.map.vars.playerType="eVar2",this.map.vars.pageName="eVar3",this.map.vars.videoName="eVar8",this.map.vars.mediaName="eVar8",this.map.vars.adTitle="eVar9",this.map.vars.searchKeyword="eVar16",this.map.vars.onsiteSearchTerm="eVar16",this.map.vars.adMode="eVar24",this.map.vars.videoSource="eVar25",this.map.vars.mediaSource="eVar25",this.map.vars.videoRepMode="eVar26",this.map.vars.mediaRepMode="eVar26",this.map.vars.onsiteSearchResults="eVar33",this.map.vars.formAnalysis="eVar34",this.map.vars.registerType="eVar37",this.map.vars.regType="eVar37",this.map.vars.videoID="eVar38",this.map.vars.mediaID="eVar38",this.map.vars.videoRepType="eVar42",this.map.vars.mediaRepType="eVar42",this.map.vars.photoURL="eVar46",this.map.vars.scrollPercent="eVar56",this.map.vars.videoOriented="eVar57",this.map.vars.buttonName="eVar58",this.map.vars.formName="eVar65",this.map.vars.adEnable="eVar67",this.map.vars.adEnabled="eVar67",this.map.vars.externalURL="eVar68",this.map.vars.externalLink="eVar68",this.map.vars.downloadLink="eVar68",this.map.vars.shareRRSS="eVar69",this.map.vars.uniqueVideoID="eVar71",this.map.vars.uniquemediaID="eVar71",this.map.vars.videoDuration="eVar74",this.map.vars.mediaDuration="eVar74",this.map.vars.videoChannels="eVar75",this.map.vars.mediaChannels="eVar75",this.map.vars.videoOrder="eVar76",this.map.vars.mediaOrder="eVar76",this.map.vars.videoCreateSection="eVar77",this.map.vars.mediaCreateSection="eVar77",this.map.vars.mediaPlayerContext="eVar78",this.map.vars.registerOrigin="eVar85",this.map.vars.registerProd="eVar86",this.map.vars.videoYoutubeChannel="eVar95",this.map.vars.videoIframe="eVar98",this.map.vars.mediaIframe="eVar98",this.map.vars.videoContractID="eVar99",this.map.vars.mediaContractID="eVar99",this.map.vars.paywallTransactionType="eVar152",this.map.vars.noticeName="eVar155",this.map.vars.pageNameEP="eVar166",this.map.vars.pageTitleEP="eVar170",this.map.vars.registerBackURL="eVar175",this.map.vars.gameName="eVar176",this.map.vars.gameID="eVar177",this.map.vars.swipeMod="eVar183",this.map.vars.swipeDir="eVar184",this.map.vars.mediaReelPosition="eVar188",this.map.vars.popupName="prop9"},getDL:function(){return this.dl},setDL:function(e){this.dl=e},isEnabled:function(){var e=void 0!==DTM.config.omn_enabled?DTM.config.omn_enabled:DTM.tools.allowAll;return e&&_satellite.getVar("platform")==DTM.PLATFORM.WIDGET&&(e=!1),e=e?DTM.tools.ENABLED:DTM.tools.DISABLED},initTracker:function(){DTM.s=window.s,"production"!=_satellite.environment.stage||_satellite.getVar("validPage")||(s.account="prisacomfiltradourls"),DTM.s.debugTracking=!1,DTM.s.dstStart=_satellite.getVar("date:dstStart"),DTM.s.dstEnd=_satellite.getVar("date:dstEnd"),DTM.s.currentYear=_satellite.getVar("date:year"),DTM.s.cookieDomainPeriods=document.URL.indexOf(".com.")>0?"3":"2",DTM.s.siteID=_satellite.getVar("siteID"),DTM.s.trackInlineStats=!0,DTM.s.linkTrackVars="None",DTM.s.linkTrackEvents="None"},formatListVar:function(e,t){if("string"==typeof e)return e.replace(/,;|,/g,";").replace(/^;/,"");var a=[];t=void 0===t?"id":t;try{for(var r=0,i=e.length;r<i;r++)"id"==t&&""!=e[r][t]?a.push(e[r][t]):"id"==t&&e[r].hasOwnProperty("name")&&a.push(e[r].name.toLowerCase().replace(/ /g,"_").replace(/\xe1/gi,"a").replace(/\xe9/gi,"e").replace(/\xf3/gi,"o").replace(/\xed/gi,"i").replace(/\xfa/gi,"u").replace(/\xf1/gi,"n")+"_a")}catch(e){a=[]}return"id"==t?a.join(";"):a.join(",")},trackPV:function(e){if(this.enabled!=DTM.tools.ENABLED||void 0===e&&this.trackedPV)return!1;for(var t in _satellite.getVar("platform")!=DTM.PLATFORM.FBIA&&!0!==e||(DTM.s.pageURL=_satellite.getVar("destinationURL"),DTM.s.referrer=_satellite.getVar("referringURL")),DTM.s.dstStart=_satellite.getVar("date:dstStart"),DTM.s.dstEnd=_satellite.getVar("date:dstEnd"),DTM.s.currentYear=_satellite.getVar("date:year"),DTM.s.siteID=_satellite.getVar("siteID"),DTM.s.pageName=_satellite.getVar("pageName"),DTM.s.channel=_satellite.getVar("primaryCategory"),DTM.s.server=_satellite.getVar("server"),DTM.s.pageType="error-404"==_satellite.getVar("primaryCategory")?"errorPage":"",DTM.s.hier1='D=c18+">"+c19+">"+c20+">"+c1+">"pageName',DTM.s.list1=_satellite.getVar("omniture:tags"),DTM.s.list2=_satellite.getVar("omniture:author"),DTM.s.list3=_satellite.getVar("omniture:secondaryCategories"),DTM.s.campaign||(DTM.s.campaign=_satellite.getVar("campaign"),DTM.s.campaign=DTM.s.getValOnce(DTM.s.campaign,"s_campaign",0)),DTM.s.prop1=_satellite.getVar("subCategory1"),DTM.s.prop2=_satellite.getVar("subCategory2"),void 0!==_satellite.getVar("pageTypology")&&""!=_satellite.getVar("pageTypology")?DTM.s.prop3=_satellite.getVar("pageType")+">"+_satellite.getVar("pageTypology"):DTM.s.prop3=_satellite.getVar("pageType"),DTM.s.prop5="D=g",DTM.s.prop6="D=r",DTM.s.prop7=_satellite.getVar("referringDomain"),DTM.s.prop10=_satellite.getVar("articleLength"),DTM.s.prop16=_satellite.getVar("onsiteSearchTerm"),DTM.s.prop17=_satellite.getVar("sysEnv"),DTM.s.prop19=_satellite.getVar("publisher"),DTM.s.prop20=_satellite.getVar("domain"),DTM.s.prop21=_satellite.getVar("omniture:newRepeat"),DTM.s.prop23=_satellite.getVar("articleID"),DTM.s.prop28=_satellite.getVar("omniture:visitNumDay"),DTM.s.prop31=_satellite.getVar("thematic"),DTM.s.prop34=_satellite.getVar("user:profileID"),DTM.s.prop39=_satellite.getVar("articleTitle"),DTM.s.prop42=_satellite.getVar("user:type"),"suscriptorT2"==DTM.s.prop42&&(DTM.s.prop42="suscriptor"),DTM.s.prop44=_satellite.getVar("creationDate"),DTM.s.prop45=_satellite.getVar("pageTitle"),DTM.s.prop47=_satellite.getVar("edition"),DTM.s.prop49=_satellite.getVar("liveContent"),DTM.s.prop50=_satellite.getVar("cms"),DTM.s.prop51=_satellite.getVar("omniture:brandedContent"),DTM.s.prop53=_satellite.getVar("canonicalURL"),DTM.s.prop54=_satellite.getVar("clickOrigin"),DTM.s.prop61=_satellite.getVar("editionNavigation"),DTM.s.prop66=_satellite.getVar("loadType"),DTM.s.prop67=DTM.utils.checkShownBlock(),DTM.s.prop68=DTM.utils.checkOriginBlock(),DTM.s.prop72=_satellite.getVar("omniture:articleDays"),void 0!==window.pmUserComparison&&(DTM.s.prop69=window.pmUserComparison.replace("OK","PMUser|OK")),this.map.vars)DTM.s[this.map.vars[t]]="" ;for(var a in DTM.s.eVar1="D=g",DTM.s.eVar3="D=pageName",DTM.s.eVar4="D=ch",DTM.s.eVar5=DTM.s.prop1?"D=c1":"",DTM.s.eVar6=DTM.s.prop2?"D=c2":"",DTM.s.eVar7=DTM.s.prop3?"D=c3":"",DTM.s.eVar10=DTM.s.prop10?"D=c10":"",DTM.s.eVar16=DTM.s.prop16?"D=c16":"",DTM.s.eVar17=DTM.s.prop17?"D=c17":"",DTM.s.eVar19=DTM.s.prop19?"D=c19":"",DTM.s.eVar20=DTM.s.prop20?"D=c20":"",DTM.s.eVar21=DTM.s.prop21?"D=c21":"",DTM.s.eVar23=DTM.s.prop23?"D=c23":"",DTM.s.eVar27=_satellite.getVar("cleanURL"),DTM.s.eVar28=DTM.s.prop28?"D=c28":"",DTM.s.eVar31=_satellite.getVar("pageInstanceID"),DTM.s.eVar33=_satellite.getVar("onsiteSearchResults"),DTM.s.eVar36=_satellite.getVar("omniture:registeredUserAMP"),DTM.s.eVar39=DTM.s.prop39?"D=c39":"",DTM.s.eVar41=_satellite.getVar("publisherID"),DTM.s.eVar43=DTM.s.prop34?"D=c34":"",DTM.s.eVar44=DTM.s.prop44?"D=c44":"",DTM.s.eVar45=_satellite.getVar("pageTitle"),DTM.s.eVar47=DTM.s.prop47?"D=c47":"",DTM.s.eVar49=DTM.s.prop49?"D=c49":"",DTM.s.eVar50=DTM.s.prop50?"D=c50":"",DTM.s.eVar51=DTM.s.prop51?"D=c51":"",DTM.s.eVar53=DTM.s.prop53?"D=c53":"",DTM.s.eVar54=DTM.s.prop54?"D=c54":"",DTM.s.eVar55=_satellite.getVar("omniture:videoContent"),DTM.s.eVar59=_satellite.getVar("editorialTone"),DTM.s.eVar61=DTM.s.prop61?"D=c61":"",DTM.s.eVar62=DTM.s.prop31?"D=c31":"",DTM.s.eVar63=DTM.s.prop6?DTM.s.prop6:"",DTM.s.eVar64=DTM.s.prop7?"D=c7":"",DTM.s.eVar66=DTM.s.prop66?"D=c66":"",DTM.s.eVar72=DTM.s.prop72?"D=c72":"",DTM.s.eVar73=_satellite.getVar("test"),DTM.s.eVar81="D=mid",DTM.s.eVar83=DTM.utils.getQueryParam("mid"),DTM.s.eVar84=DTM.utils.getQueryParam("bid"),DTM.s.eVar85=DTM.utils.getQueryParam("o"),DTM.s.eVar86=DTM.utils.getQueryParam("prod"),DTM.s.eVar92=_satellite.getVar("user:type"),DTM.s.eVar93=_satellite.getVar("user:ID"),DTM.s.eVar94=_satellite.getVar("updateDate"),DTM.s.eVar96=_satellite.getVar("pageHeight"),DTM.s.eVar100=_satellite.getVar("publishDate"),DTM.s.eVar101=_satellite.getVar("DTM:version"),DTM.s.eVar102=_satellite.getVar("AppMeasurement:version"),DTM.s.eVar103=_satellite.getVar("Visitor:version"),DTM.s.eVar104=_satellite.getVar("omniture:trackingServer"),DTM.s.eVar105=DTM.dataLayer.sync,DTM.s.eVar106=DTM.internalTest,DTM.s.eVar107=_satellite.getVar("adunit:pbs"),DTM.s.eVar109=_satellite.getVar("user:subscriptionType"),DTM.s.eVar110=_satellite.getVar("paywall:id"),DTM.s.eVar112=_satellite.getVar("urlParameters"),DTM.s.eVar151=_satellite.getVar("paywall:signwallType"),DTM.s.eVar152=_satellite.getVar("paywall:transactionType"),DTM.s.eVar153=_satellite.getVar("omniture:paywall:contentBlocked"),DTM.s.eVar154=_satellite.getVar("paywall:counter"),DTM.s.eVar155=_satellite.getVar("paywall:contentAdType"),DTM.s.eVar156=_satellite.getVar("user:subscriptions"),DTM.s.eVar157=_satellite.getVar("omniture:paywall:active"),DTM.s.eVar158="epmas>suscripcion>confirmation"==_satellite.getVar("subCategory2")?_satellite.getVar("paywall:transactionID"):"",DTM.s.eVar161=_satellite.getVar("omniture:privateMode"),DTM.s.eVar162=_satellite.getVar("paywall:transactionOrigin"),DTM.s.eVar166=_satellite.getVar("pageName"),DTM.s.eVar170=_satellite.getVar("pageTitle"),DTM.s.eVar193=_satellite.getVar("paywall:type"),"suscriptorT2"==DTM.s.eVar92&&(DTM.s.eVar92="suscriptor"),!0===e&&(DTM.s.products=""),"not-set"!=_satellite.getVar("paywall:cartProduct")&&-1!=_satellite.getVar("omniture:cartProductPages").indexOf(_satellite.getVar("subCategory2"))&&(DTM.s.products=";"+_satellite.getVar("paywall:cartProduct")+";1;"),"epmas>suscripcion>confirmation"!=_satellite.getVar("subCategory2")&&"epmas>suscripcion>premium_confirmation"!=_satellite.getVar("subCategory2")||(DTM.s.purchaseID=_satellite.getVar("paywall:transactionID")),DTM.s.events="event2","1"==_satellite.getVar("onsiteSearch")&&(DTM.s.events+=",event1"),"articulo"==_satellite.getVar("pageType")&&(DTM.s.events+=",event77"),"epmas>suscripcion>home"!=_satellite.getVar("subCategory2")&&"epmas>landing_campaign_premium_user"!=_satellite.getVar("subCategory2")||(DTM.s.events+=",event59"),"epmas>suscripcion>checkout"==_satellite.getVar("subCategory2")&&(DTM.s.events+=",scCheckout,event60"),("epmas>suscripcion>confirmation"!=_satellite.getVar("subCategory2")&&"epmas>suscripcion>premium_confirmation"!=_satellite.getVar("subCategory2")||""==_satellite.getVar("paywall:transactionID"))&&"epmas>upgrade_premium>confirmation"!=_satellite.getVar("subCategory2")||(DTM.s.events+=",purchase,event61"),-1!=_satellite.getVar("subCategory2").indexOf("epmas>suscripcion>verify-gift>confirmation")&&(DTM.s.events+=",purchase,event62"),!0===_satellite.getVar("omniture:adobeTargetEnabled")&&(DTM.s.events+=",event91"),""!=_satellite.getVar("test")&&(DTM.s.events+=",event100"),DTM.s.t(),DTM.s.linkTrackEvents="None",DTM.s.linkTrackVars="None",DTM.tools.marfeel.utils.markTimeLoads("omnitureTrackedPV"),this.trackedPV=!0,this.eventQueue)this.trackEvent(a)},trackAsyncPV:function(){this.trackPV(!0)},trackEvent:function(e){if(this.enabled!=DTM.tools.DISABLED){if(this.enabled==DTM.tools.ENABLED&&!this.trackedPV)return this.eventQueue.push(e),DTM.events.setEffect(e,"omniture",!1),!1;if(void 0===_satellite.getVar("event")[e])return DTM.notify("Omniture event past not valid <"+t+">","error"),!1;var t=_satellite.getVar("event")[e].eventInfo.eventName,a=_satellite.getVar("event")[e].attributes;if(!this.map.events.hasOwnProperty(t))return DTM.events.setEffect(e,"omniture",!1),!1;var r=this.map.events[t],i=_satellite.getVar("omniture:tags"),s=void 0!==a.eventTags?this.formatListVar(a.eventTags,"id"):"";if(DTM.s.linkTrackEvents=r,DTM.s.events=r,DTM.s.server=void 0!==a.server?a.server:DTM.s.server,DTM.s.pageName=void 0!==a.pageName?a.pageName:_satellite.getVar("pageName"),DTM.s.linkTrackVars="events,server,list1,list2,list3,eVar1,eVar3,eVar4,eVar5,eVar6,eVar7,eVar10,eVar16,eVar17,eVar18,eVar19,eVar20,eVar22,eVar23,eVar30,eVar31,eVar35,eVar36,eVar39,eVar41,eVar43,eVar45,eVar47,eVar48,eVar49,eVar50,eVar51,eVar53,eVar54,eVar55,eVar59,eVar60,eVar61,eVar63,eVar64,eVar66,eVar72,eVar73,eVar81,eVar85,eVar86,eVar92,eVar93,eVar94,eVar96,eVar100,eVar101,eVar102,eVar103,eVar104,eVar106,eVar109,eVar110,eVar112,eVar151,eVar153,eVar154,eVar155,eVar156,eVar157,eVar161,eVar166,eVar170,eVar193",(a.hasOwnProperty("paywallCartProduct")||-1!=_satellite.getVar("omniture:cartProductPages").indexOf(_satellite.getVar("subCategory2")))&&(DTM.s.products=";"+(void 0!==a.paywallCartProduct?a.paywallCartProduct:_satellite.getVar("paywall:cartProduct"))+";1;",DTM.s.linkTrackVars+=",products"),DTM.s.list1=""==s?i:""==i?s:i+";"+s,DTM.s.list2=void 0!==a.authors?this.formatListVar(a.authors,"id"):_satellite.getVar("omniture:author"),DTM.s.list3=_satellite.getVar("omniture:secondaryCategories"),DTM.s.eVar1=_satellite.getVar("destinationURL"),DTM.s.eVar3=_satellite.getVar("pageName"),DTM.s.eVar4=_satellite.getVar("primaryCategory"),DTM.s.eVar5=_satellite.getVar("subCategory1"),DTM.s.eVar6=_satellite.getVar("subCategory2"),DTM.s.eVar7=_satellite.getVar("pageType"),DTM.s.eVar10=_satellite.getVar("articleLength"),DTM.s.eVar16=_satellite.getVar("onsiteSearchTerm"),DTM.s.eVar17=_satellite.getVar("sysEnv"),DTM.s.eVar19=_satellite.getVar("publisher"),DTM.s.eVar20=_satellite.getVar("domain"),DTM.s.eVar23=_satellite.getVar("articleID"),DTM.s.eVar31=_satellite.getVar("pageInstanceID"),DTM.s.eVar36=_satellite.getVar("omniture:registeredUserAMP"),DTM.s.eVar39=_satellite.getVar("articleTitle"),DTM.s.eVar41=_satellite.getVar("publisherID"),DTM.s.eVar43=_satellite.getVar("user:profileID"),DTM.s.eVar45=_satellite.getVar("pageTitle"),DTM.s.eVar47=_satellite.getVar("edition"),DTM.s.eVar49=_satellite.getVar("liveContent"),DTM.s.eVar50=_satellite.getVar("cms"),DTM.s.eVar51=_satellite.getVar("omniture:brandedContent"),DTM.s.eVar53=_satellite.getVar("canonicalURL"),DTM.s.eVar54=_satellite.getVar("clickOrigin"),DTM.s.eVar55=_satellite.getVar("omniture:videoContent"),DTM.s.eVar59=_satellite.getVar("editorialTone"),DTM.s.eVar61=_satellite.getVar("editionNavigation"),DTM.s.eVar63=_satellite.getVar("referringURL"),DTM.s.eVar64=_satellite.getVar("referringDomain"),DTM.s.eVar66=_satellite.getVar("loadType"),DTM.s.eVar72=_satellite.getVar("omniture:articleDays"),DTM.s.eVar73=_satellite.getVar("test"),DTM.s.eVar78=_satellite.getVar("mediaPlayerContext"),DTM.s.eVar81="D=mid",DTM.s.eVar85=DTM.utils.getQueryParam("o"),DTM.s.eVar86=DTM.utils.getQueryParam("prod"),DTM.s.eVar92=_satellite.getVar("user:type"),DTM.s.eVar93=_satellite.getVar("user:ID"),DTM.s.eVar94=_satellite.getVar("updateDate"),DTM.s.eVar96=_satellite.getVar("pageHeight"),DTM.s.eVar100=_satellite.getVar("publishDate"),DTM.s.eVar101=_satellite.getVar("DTM:version"),DTM.s.eVar102=_satellite.getVar("AppMeasurement:version"),DTM.s.eVar103=_satellite.getVar("Visitor:version"),DTM.s.eVar104=_satellite.getVar("omniture:trackingServer"),DTM.s.eVar106=DTM.internalTest,DTM.s.eVar109=_satellite.getVar("user:subscriptionType"),DTM.s.eVar110=_satellite.getVar("paywall:id"),DTM.s.eVar112=_satellite.getVar("urlParameters"),DTM.s.eVar151=_satellite.getVar("paywall:signwallType"),DTM.s.eVar153=_satellite.getVar("omniture:paywall:contentBlocked"),DTM.s.eVar154=_satellite.getVar("paywall:counter"),DTM.s.eVar155=_satellite.getVar("paywall:contentAdType"),DTM.s.eVar156=_satellite.getVar("user:subscriptions"),DTM.s.eVar157=_satellite.getVar("omniture:paywall:active"),DTM.s.eVar161=_satellite.getVar("omniture:privateMode"),DTM.s.eVar166=void 0!==a.pageName?a.pageName:_satellite.getVar("pageName"),DTM.s.eVar170=_satellite.getVar("pageTitle"),DTM.s.eVar193=_satellite.getVar("paywall:type"),"suscriptorT2"==DTM.s.eVar92&&(DTM.s.eVar92="suscriptor"),_satellite.getVar("event")[e]&&_satellite.getVar("event")[e].attributes&&_satellite.getVar("event")[e].attributes.mediaTagsMediateca&&_satellite.getVar("event")[e].attributes.mediaTagsMediateca.length>0){DTM.s.list1=DTM.s.list1||"",""!=DTM.s.list1&&(DTM.s.list1=DTM.s.list1+";");for(let t=0;t<_satellite.getVar("event")[e].attributes.mediaTagsMediateca.length;t++)_satellite.getVar("event")[e].attributes.mediaTagsMediateca[t].is_documental?DTM.s.list1+="multimedia-"+_satellite.getVar("event")[e].attributes.mediaTagsMediateca[t].name+";":void 0!==_satellite.getVar("event")[e].attributes.mediaTagsMediateca[t].name&&(DTM.s.list1+="multimediav-"+_satellite.getVar("event")[e].attributes.mediaTagsMediateca[t].name+";")}for(var n in a.hasOwnProperty("pageName")&&(a.pageNameEP=a.pageName),a.hasOwnProperty("pageTitle")&&(a.pageTitleEP=a.pageTitle),this.map.vars)a.hasOwnProperty(n)&&(DTM.s[this.map.vars[n]]=a[n],DTM.s.linkTrackVars+=","+this.map.vars[n]);return(DTM.s.eVar155.indexOf("capping:")>-1||DTM.s.eVar58.indexOf("capping:")>-1||DTM.s.eVar58.indexOf("popup fecha")>-1||DTM.s.eVar155.indexOf("popup fecha")>-1)&&(DTM.s.eVar108=_satellite.getVar("user:arcid"),DTM.s.linkTrackVars+=",eVar108"),t!=DTM.events.EXITLINK&&t!=DTM.events.DOWNLOADLINK&&(DTM.s.tl(this,"o",t),DTM.s.linkTrackEvents="None",DTM.s.linkTrackVars="None"),DTM.notify("Event <"+t+"> tracked in tool <Adobe Analytics>"),DTM.events.setEffect(e,"omniture",!0),!0}}},gfk:{enabled:1,dl:{},trackedPV:!1,init:function(){DTM.tools.marfeel.utils.markTimeLoads("GFK init"),DTM.tools.gfk.enabled=DTM.tools.gfk.isEnabled(),DTM.tools.gfk.enabled==DTM.tools.ENABLED&&DTM.tools.list.push("gfk"),DTM.tools.gfk.setDL({mediaID:_satellite.getVar("publisherID"),regionID:"ES",hosts:{staging:"ES-config-preproduction.sensic.net",production:"ES-config.sensic.net"},environment:"production"!=_satellite.environment.stage||!_satellite.getVar("validPage")||_satellite.getVar("translatePage")?"staging":"production",libs:{page:"s2s-web.js",html5:"html5vodextension.js",html5live:"html5liveextension.js",youtube:"youtubevodextension.js",playerextension:"playerextension.js"},url:"",type:"WEB",optin:!0,logLevel:"none"}),DTM.tools.gfk.trackPV()},getDL:function(){return this.dl},setDL:function(e){this.dl=e},isEnabled:function(){var e=void 0!==DTM.config.gfk_enabled?DTM.config.gfk_enabled:DTM.tools.allowAll;return e&&_satellite.getVar("platform")!=DTM.PLATFORM.WEB&&(e=!1),e=e?DTM.tools.ENABLED:DTM.tools.DISABLED},trackPV:function(){if(this.enabled!=DTM.tools.ENABLED||!0===this.trackedPV)return!1;this.getDL();this.loadCoreLib();var e=gfkS2s.getAgent(),t={c1:_satellite.getVar("server"),c2:this.getPrimaryCategory()};e.impression("default",t),DTM.tools.marfeel.utils.markTimeLoads("gfkTrackedPV"),this.trackedPV=!0},trackAsyncPV:function(){if(this.enabled!=DTM.tools.ENABLED)return!1;var e=gfkS2s.getAgent(),t={c1:_satellite.getVar("server"),c2:this.getPrimaryCategory()};e.impression("default",t),this.trackedPV=!0},trackEvent:function(e){if(this.enabled==DTM.tools.DISABLED)return DTM.events.setEffect(e,"gfk",!1),!1;if(void 0===_satellite.getVar("event")[e])return DTM.notify("GFK event past not valid <"+t+">","error"),!1;var t=_satellite.getVar("event")[e].eventInfo.eventName,a=_satellite.getVar("event")[e].attributes,r=!1;switch(t){case"photogallery":case"scrollInf":var i=gfkS2s.getAgent(),s={c1:_satellite.getVar("server"),c2:this.getPrimaryCategory()};i.impression("default",s),r=!0;break;case"videoReady":case"audioReady":if(!a.hasOwnProperty("player")||!a.hasOwnProperty("mediaID")||this.streaming.myStreamingAnalytics.hasOwnProperty(a.mediaID))return!1;r=this.streaming.init(t,a);break;case"videoPlay":case"reelPlay":case"videoResumed":if(!a.hasOwnProperty("mediaID")||!this.streaming.myStreamingAnalytics.hasOwnProperty(a.mediaID))return!1;r=this.streaming.play(t,a);break;case"videoPaused":case"reelEnd":case"videoEnd":if(!a.hasOwnProperty("mediaID")||!this.streaming.myStreamingAnalytics.hasOwnProperty(a.mediaID))return!1;r=this.streaming.pause(t,a);break;case"videoSeekInit":case"videoSeekComplete":if(!a.hasOwnProperty("mediaID")||!this.streaming.myStreamingAnalytics.hasOwnProperty(a.mediaID))return!1;r=this.streaming.seek(t,a);break;default:r=!1}return!0===r&&DTM.notify("Event <"+t+"> tracked in tool <GFK>"),DTM.events.setEffect(e,"gfk",r),r},getLibURL:function(e){var t=!1,a=this.dl,r=a.hosts[a.environment];return a.libs.hasOwnProperty(e)&&(t="https://"+r+"/"+a.libs[e]),t},getPrimaryCategory:function(){var e="";if(""!=_satellite.getVar("primaryCategory"))e=_satellite.getVar("primaryCategory"),"home"==_satellite.getVar("primaryCategory")?e="homepage":"tag"==_satellite.getVar("primaryCategory")&&(e="noticias");else{var t=/http.?:\/\/([^\/]*)\/([^\/]*)\//i.exec(_satellite.getVar("destinationURL"));e=t?t[2]:"homepage"}return e},loadCoreLib:function(){var e=this.getDL();window.gfkS2sConf={media:e.mediaID,url:this.getLibURL("page"),type:e.type};var t=window,a=document,r=gfkS2sConf,i="script",s="gfkS2s",n="visUrl";if(!a.getElementById(s)){t.gfkS2sConf=r,t[s]={},t[s].agents=[];var o=["playStreamLive","playStreamOnDemand","stop","skip","screen","volume","impression"];t.gfks=function(){function e(e,t,a){return function(){e.p=a(),e.queue.push({f:t,a:arguments})}}function t(t,a,r){for(var i={queue:[],config:t,cb:r,pId:a},s=0;s<o.length;s++){var n=o[s];i[n]=e(i,n,r)}return i}return t}(),t[s].getAgent=function(e,a){function i(e,t){return function(){return e.a[t].apply(e.a,arguments)}}for(var n={a:new t.gfks(r,a||"",e||function(){return 0})},l=0;l<o.length;l++){var d=o[l];n[d]=i(n,d)}return t[s].agents.push(n),n};var l=function(e,t){var r=a.createElement(i),s=a.getElementsByTagName(i)[0];r.id=e,r.async=!0,r.type="text/javascript",r.src=t,s.parentNode.insertBefore(r,s)};r.hasOwnProperty(n)&&l(s+n,r[n]),l(s,r.url)}},streaming:{myStreamingAnalytics:[],libsLoaded:{html5:!1,html5live:!1,youtube:!1,playerextension:!1},loadLib:function(e,t,a){if(_satellite.getVar("platform")!=DTM.PLATFORM.WEB)return!1;if(this.libsLoaded.hasOwnProperty(e)&&!1===this.libsLoaded[e]){var r=DTM.tools.gfk.getLibURL(e);DTM.utils.loadScript(r,t,a)}else this.libsLoaded.hasOwnProperty(e)&&!0===this.libsLoaded[e]&&t.call(this,a)},init:function(e,t){var a=!1,r=t.player,i=t.hasOwnProperty("mediaName")?t.mediaName:r.hasOwnProperty("title")?r.title:"",s=_satellite.getVar("publisher")+"-"+i,n=t.hasOwnProperty("mediaDuration")?t.mediaDuration:r.hasOwnProperty("duration")?parseInt(r.duration):"",o=t.hasOwnProperty("playerType")?DTM.utils.getPlayerType(t.playerType):"html5";o=t.controllerName?t.controllerName:o;var l=t.hasOwnProperty("mediaRepType")?t.mediaRepType:"vod",d=t.hasOwnProperty("mediaFormat")?t.mediaFormat:r.hasOwnProperty("mediaFormat")?r.mediaFormat:"";switch(o){case"html5":case"realhls":if("streaming"==l)this.loadLib("html5live",(function(e){DTM.tools.gfk.streaming.libsLoaded.html5live=!0,DTM.tools.gfk.streaming.myStreamingAnalytics[e.mediaID]={gfkObject:new window.gfkS2sExtension.HTML5LiveExtension(e.player,window.gfkS2sConf,"default",{programmname:e.mediaName,channelname:_satellite.getVar("publisher"),streamtype:d,c1:_satellite.getVar("server"),c2:DTM.tools.gfk.getPrimaryCategory()}),player:r}}),{mediaID:t.mediaID,player:r,streamtype:d,mediaName:s,mediaDuration:n}),a=!0;else{if(""==d&&"aod"==l){if(d="audio",void 0!==window.mediaTopEmbedCs&&void 0!==window.mediaTopEmbedCs.API&&void 0!==window.mediaTopEmbedCs.API.getSettings()){var c=window.mediaTopEmbedCs.API.getSettings();s=_satellite.getVar("publisher")+"-"+c.topPlayer.media.tags.programa}}else""==d&&"vod"==l&&(d="video");this.loadLib("html5",(function(e){DTM.tools.gfk.streaming.libsLoaded.html5=!0,DTM.tools.gfk.streaming.myStreamingAnalytics[e.mediaID]={gfkObject:new 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e.player.getState()};DTM.tools.gfk.streaming.myStreamingAnalytics[e.mediaID]={gfkObject:new window.gfkS2sExtension.PlayerExtension(t,window.gfkS2sConf,"default",{programmname:e.mediaName,channelname:_satellite.getVar("publisher"),streamtype:d,streamlength:e.mediaDuration,c1:_satellite.getVar("server"),c2:DTM.tools.gfk.getPrimaryCategory()}),player:e.player}}),{mediaID:t.mediaID,player:r,streamtype:d,mediaName:s,mediaDuration:n}),a=!0);break;default:a=!1}return a},play:function(e,t){var a=t.hasOwnProperty("playerType")?DTM.utils.getPlayerType(t.playerType):"html5",r=!1;if("youtube"==a&&"videoPlay"==e){let e=this.myStreamingAnalytics[t.mediaID].gfkObject,a=this.myStreamingAnalytics[t.mediaID].player,r=_satellite.getVar("publisher")+"_"+t.hasOwnProperty("mediaName")?t.mediaName:a.hasOwnProperty("videoTitle")?a.videoTitle:"",i=t.hasOwnProperty("mediaDuration")?t.mediaDuration:"function"==typeof a.getDuration?parseInt(a.getDuration()):"",s=t.hasOwnProperty("mediaFormat")?t.mediaFormat:a.hasOwnProperty("mediaFormat")?a.mediaFormat:"";e.setParameter("default",{programmname:r,channelname:_satellite.getVar("publisher"),streamtype:s,streamlength:i,c1:_satellite.getVar("server"),c2:DTM.tools.gfk.getPrimaryCategory()})}else if("triton"==a||"ser_especial"==a){let e=this.myStreamingAnalytics[t.mediaID].gfkObject,a=this.myStreamingAnalytics[t.mediaID].player,s=t.hasOwnProperty("mediaDuration")?t.mediaDuration:a.hasOwnProperty("duration")?parseInt(a.duration):"",n=t.hasOwnProperty("mediaFormat")?t.mediaFormat:a.hasOwnProperty("mediaFormat")?a.mediaFormat:"";if("streaming"==t.mediaRepType)var i=_satellite.getVar("publisher")+"-"+t.mediaName;else i=_satellite.getVar("publisher")+"-"+t.hasOwnProperty("mediaName")?t.mediaName:a.hasOwnProperty("videoTitle")?a.videoTitle:"";a.dtm_status="playing",t.hasOwnProperty("mediaRepType")&&"streaming"==t.mediaRepType?e.playStreamLive("default","",0,t.mediaID,{},{programmname:i,channelname:_satellite.getVar("publisher"),streamtype:n,cliptype:"live",channel:"channel1",c1:_satellite.getVar("server"),c2:DTM.tools.gfk.getPrimaryCategory()}):e.playStreamOnDemand("default",t.mediaID,{},{programmname:i,streamlength:s,channelname:_satellite.getVar("publisher"),streamtype:n,cliptype:"Sendung",channel:"channel1",c1:_satellite.getVar("server"),c2:DTM.tools.gfk.getPrimaryCategory()}),r=!0}return r},pause:function(e,t){var a=!1;if("dailymotion"!=(t.hasOwnProperty("playerType")?DTM.utils.getPlayerType(t.playerType):"html5"))return a;var r=this.myStreamingAnalytics[t.mediaID].gfkObject;return this.myStreamingAnalytics[t.mediaID].player.dtm_status="paused",r.stop(),a=!0},seek:function(e,t){var a=!1;if("dailymotion"!=(t.hasOwnProperty("playerType")?DTM.utils.getPlayerType(t.playerType):"html5"))return a;if("videoSeekInit"==e){var r=this.myStreamingAnalytics[t.mediaID].gfkObject;"playing"==(i=this.myStreamingAnalytics[t.mediaID].player).dtm_status&&(r.stop(),a=!0)}else if("videoSeekComplete"==e){r=this.myStreamingAnalytics[t.mediaID].gfkObject;var i=this.myStreamingAnalytics[t.mediaID].player,s=t.hasOwnProperty("mediaName")?t.mediaName:i.hasOwnProperty("title")?i.title:"",n=t.hasOwnProperty("mediaDuration")?t.mediaDuration:i.hasOwnProperty("duration")?parseInt(i.duration):"";i.getState().then((e=>{var t=JSON.parse(JSON.stringify(e));i.dtm_currentTime=1e3*parseInt(t.videoTime)})),"playing"==i.dtm_status&&(r.playStreamOnDemand("default",t.mediaID,{},{programmname:s,streamlength:n,channelname:_satellite.getVar("publisher"),cliptype:"Sendung",channel:"channel1",airdate:new Date,c1:_satellite.getVar("server"),c2:DTM.tools.gfk.getPrimaryCategory()}),a=!0)}return a}}},marfeel:{enabled:1,dl:{proId:"2223",environment:"",filterId:"1059",contentVisibility:"",mapEvents:{adPlay:"adPlay",videoPlay:"play",reelPlay:"play",videoResumed:"play",videoPaused:"pause",videoEnd:"end",reelEnd:"end",audioPlay:"play",audioPaused:"pause",audioResumed:"play",audioEnd:"end"},mediaControls:{},mediaReady:{}},lib:{init:function(){function e(e){var t=!(arguments.length>1&&void 0!==arguments[1])||arguments[1],a=document.createElement("script");a.src=e,t?a.type="module":(a.async=!0,a.type="text/javascript",a.setAttribute("nomodule",""));var r=document.getElementsByTagName("script")[0];r.parentNode.insertBefore(a,r)}function t(t,a,r){var i,s,n;null!==(i=t.marfeel)&&void 0!==i||(t.marfeel={}),null!==(s=(n=t.marfeel).cmd)&&void 0!==s||(n.cmd=[]),t.marfeel.config=r,t.marfeel.config.accountId=a;var o="https://sdk.mrf.io/statics";e("".concat(o,"/marfeel-sdk.js?id=").concat(a),!0),e("".concat(o,"/marfeel-sdk.es5.js?id=").concat(a),!1)}DTM.tools.marfeel.utils.markTimeLoads("MArfeel lib init");var a=DTM.tools.marfeel.dl;!function(e,a){t(e,a,arguments.length>2&&void 0!==arguments[2]?arguments[2]:{})}(window,a.environment,{pageType:_satellite.getVar("platform"),multimedia:{},experiences:{targeting:DTM.utils.getMarfeelExp()}}),DTM.tools.marfeel.ABTesting()},testab:function(e){var t=DTM.tools.marfeel.dl,a="",r=document.querySelector("link[rel='canonical']")?document.querySelector("link[rel='canonical']").getAttribute("href"):_satellite.getVar("canonicalURL");return"module"==e?a="https://marfeelexperimentsexperienceengine.mrf.io/experimentsexperience/render?siteId="+t.environment+"&url="+r+"&experimentType=HeadlineAB&lang=es&version=esnext":"nomodule"==e&&(a="https://marfeelexperimentsexperienceengine.mrf.io/experimentsexperience/render?siteId="+t.environment+"&url="+r+"&experimentType=HeadlineAB&lang=es&version=legacy"),a}},trackedPV:!1,init:function(){DTM.tools.marfeel.utils.markTimeLoads("MArfeel init"),"fbia"==_satellite.getVar("platform")&&(window.ia_document={shareURL:_satellite.getVar("destinationURL"),referrer:_satellite.getVar("referringURL")}),this.enabled=this.isEnabled();var e=DTM.tools.marfeel.dl;"production"!=_satellite.environment.stage||!_satellite.getVar("validPage")||_satellite.getVar("translatePage")?this.dl.environment=e.filterId:this.dl.environment=e.proId,null!=_satellite.getVar("paywall:active")&&null!=_satellite.getVar("paywall:signwallType")&&(e.contentVisibility=_satellite.getVar("paywall:active")&&"suscriptor"!=_satellite.getVar("user:type")?"hard-paywall":"",e.contentVisibility=_satellite.getVar("paywall:signwallType").indexOf("reg")>-1&&"1"==_satellite.getVar("paywall:contentBlocked")?"dynamic-signwall":""),this.enabled!=DTM.tools.DISABLED&&(DTM.tools.list.push("marfeel"),this.lib.init())},trackPV:function(){var e=0;switch(_satellite.getVar("user:type")){case"suscriptor":e=3;break;case"registrado":e=2}window.marfeel.cmd.push(["compass",function(t){t.setUserType(e),void 0!==_satellite.getVar("user:profileID")&&"anonimo"!=_satellite.getVar("user:type")&&"undefined"!=_satellite.getVar("user:profileID")&&"not-set"!=_satellite.getVar("user:profileID")&&""!=_satellite.getVar("user:profileID")&&t.setSiteUserId(_satellite.getVar("user:profileID")),_satellite.getVar("user:experienceCloudID")&&t.setUserVar("ecid",_satellite.getVar("user:experienceCloudID")),""!=DTM.tools.marfeel.dl.contentVisibility&&null!=DTM.tools.marfeel.dl.contentVisibility&&t.setPageVar("closed",DTM.tools.marfeel.dl.contentVisibility),"T1"!=_satellite.getVar("user:subscriptionType")&&"T2"!=_satellite.getVar("user:subscriptionType")?t.setUserVar("subscriberType","not-set"):t.setUserVar("subscriberType",_satellite.getVar("user:subscriptionType")),t.setPageVar("sub-section",_satellite.getVar("subCategory1")),t.setPageVar("sub-sub-section",_satellite.getVar("subCategory2")),t.setPageVar("contentType",_satellite.getVar("pageType")),t.setPageVar("organizacion",_satellite.getVar("org")),t.setPageVar("producto-medio",_satellite.getVar("publisher")),t.setPageVar("domain",_satellite.getVar("domain")),t.setUserVar("usuario-recurrente",_satellite.getVar("omniture:newRepeat")),t.setPageVar("noticia-id",_satellite.getVar("articleID")),t.setPageVar("id-instancia",_satellite.getVar("pageInstanceID")),t.setUserVar("user-id",_satellite.getVar("user:profileID")),t.setPageVar("edicion-contenido",_satellite.getVar("edition")),t.setPageVar("cms",_satellite.getVar("cms")),t.setPageVar("edicion-navegacion",_satellite.getVar("editionNavigation")),t.setPageVar("tematica",_satellite.getVar("thematic")),t.setPageVar("cms",_satellite.getVar("loadType")),t.setUserVar("user-arc-id",_satellite.getVar("user:ID"));try{_satellite.getVar("subCategory2").indexOf("epmas")>-1&&_satellite.getVar("subCategory2").indexOf("confirmation")>-1&&-1==_satellite.getVar("subCategory2").indexOf("invitation")&&-1==_satellite.getVar("subCategory2").indexOf("verify-gift")&&(t.setPageVar("test_DTM",_satellite.getVar("subCategory2")),DTM.trackEvent("userSubscription",{}))}catch(e){}}]);var t=JSON.parse(localStorage.getItem("No_Consent")),a=Date.now();return null!=t&&Object.keys(t).forEach((e=>{var r=new Date(t[e].creation);(r=r.getTime())+24*parseInt(t[e][e+"_expiration"])*60*60*1e3<a&&delete t[e]})),localStorage.setItem("No_Consent",JSON.stringify(t)),DTM.tools.marfeel.utils.markTimeLoads("marfeelTrackedPV"),this.trackedPV=!0,DTM.notify("PV tracked in tool <marfeel> (Data Layer)"),!0},trackAsyncPV:function(){if(this.enabled==DTM.tools.DISABLED)return!1;this.trackPV()},trackEvent:function(e){if(this.enabled==DTM.tools.DISABLED)return DTM.events.setEffect(e,"marfeel",!1),!1;if(void 0===_satellite.getVar("event")[e])return DTM.notify("Marfeel event past not valid <"+t+">","error"),!1;var t=_satellite.getVar("event")[e].eventInfo.eventName,a=_satellite.getVar("event")[e].attributes;switch("T1"!=_satellite.getVar("user:subscriptionType")&&"T2"!=_satellite.getVar("user:subscriptionType")?window.marfeel.cmd.push(["compass",function(e){e.setUserVar("subscriberType","not-set")}]):window.marfeel.cmd.push(["compass",function(e){e.setUserVar("subscriberType",_satellite.getVar("user:subscriptionType"))}]),t){case"userNewsletterIN":window.marfeel.cmd.push(["compass",function(e){var t="";for(code in a.newsletters)t=t+" "+a.newsletters[codes];e.trackNewPage({rs:"userNewsletterIN "+t})}]),DTM.notify("Event <"+t+"> tracked in tool <Marfeel>"),DTM.events.setEffect(e,"marfeel",!0);break;case"userLogin":window.marfeel.cmd.push(["compass",function(e){e.trackNewPage({rs:"userLogin"})}]),DTM.notify("Event <"+t+"> tracked in tool <Marfeel>"),DTM.events.setEffect(e,"marfeel",!0);break;case"userRegister":window.marfeel.cmd.push(["compass",function(e){e.trackNewPage({rs:"userRegister"})}]),DTM.notify("Event <"+t+"> tracked in tool <Marfeel>"),DTM.events.setEffect(e,"marfeel",!0);break;case"audioReady":case"videoReady":void 0===DTM.tools.marfeel.dl.mediaReady[a.mediaID]&&(window.marfeel.cmd.push(["multimedia",function(e){var r="";null==a.mediaID&&null!=a.mediaId&&(a.mediaID=a.mediaId),r=null==a.mediaFormat?"audioReady"==t?"audio":"videoReady"==t?"video":"not-set":a.mediaFormat,"streaming"==a.mediaRepType&&(a.mediaDuration=-1),e.initializeItem(null!=a.mediaID?a.mediaID:"not-set",DTM.utils.getPlayerType(a.playerType),null!=a.mediaID?a.mediaID:"not-set",r,{isLive:null!=a.mediaRepType&&"streaming"==a.mediaRepType,title:null!=a.mediaName?a.mediaName:"not-set",description:null!=a.mediaName?a.mediaName:"not-set",url:null!=a.mediaUrl?a.mediaUrl:"not-set",thumbnail:null!=a.mediaThumbnail?a.mediaThumbnail:"not-set",authors:null!=a.mediaAuthors?a.mediAuthors:"not-set",publishTime:null!=a.mediaPlublishTime?a.mediaPlublishTime:"not-set",duration:null!=a.mediaDuration?a.mediaDuration:"not-set"})}]),DTM.tools.marfeel.dl.mediaReady[a.mediaID]=!0,DTM.events.setEffect(e,"marfeel",!0),DTM.notify("Event <"+t+"> tracked in tool <Marfeel>"));break;case"adPlay":case"videoPlay":case"reelPlay":case"videoPaused":case"videoResumed":case"videoEnd":case"reelEnd":case"audioPlay":case"audioResumed":case"audioPaused":case"audioEnd":if(null==a.mediaID&&null==a.mediaId)return!1;null==a.mediaID&&null!=a.mediaId&&(a.mediaID=a.mediaId),void 0!==DTM.tools&&void 0!==DTM.tools.marfeel&&void 0!==DTM.tools.marfeel.dl&&void 0!==DTM.tools.marfeel.dl.mediaReady&&void 0!==DTM.tools.marfeel.dl.mediaReady[a.mediaID]?(window.marfeel.cmd.push(["multimedia",function(e){e.registerEvent(a.mediaID,DTM.tools.marfeel.dl.mapEvents[t],parseInt(a.currentTime))}]),void 0===DTM.tools.marfeel.dl.mediaControls[a.mediaID]?"audioPlay"!=t&&"videoPlay"!=t&&"reelPlay"!=t&&"audioResumed"!=t&&"videoResumed"!=t&&"adEnd"!=t||DTM.tools.marfeel.utils.mediaIntervals(a.mediaID,"set",parseInt(a.currentTime)):"audioPaused"!=t&&"videoPaused"!=t&&"audioEnd"!=t&&"videoEnd"!=t&&"reelEnd"!=t&&"adPlay"!=t||DTM.tools.marfeel.utils.mediaIntervals(a.mediaID,"clear"),DTM.events.setEffect(e,"marfeel",!0),DTM.notify("Event <"+t+"> tracked in tool <Marfeel>")):DTM.notify("Alert evento Media sin Ready en tool <Marfeel>");break;case"share":window.marfeel.cmd.push(["compass",function(e){e.setPageVar("share",a.shareRRSS)}]),DTM.events.setEffect(e,"marfeel",!0),DTM.notify("Event <"+t+"> tracked in tool <Marfeel>");break;case"photogallery":window.marfeel.cmd.push(["compass",function(e){e.trackConversion("photogallery")}]),DTM.events.setEffect(e,"marfeel",!0),DTM.notify("Event <"+t+"> tracked in tool <Marfeel>");break;case"userSubscription":var r={"epmas>suscripcion>confirmation":"basica","epmas>suscripcion>premium_confirmation":"premium","epmas>upgrade_premium>confirmation":"upgrade"};window.marfeel.cmd.push(["compass",function(e){e.setPageVar("test_DTM",_satellite.getVar("subCategory2")),e.setPageVar("tipoSuscripcion",r[_satellite.getVar("subCategory2")]),e.trackConversion("subscribe"),DTM.notify("Event <userSubscription> tracked in tool <Marfeel>")}]);break;default:return DTM.events.setEffect(e,"marfeel",!1),!1}return!0},isEnabled:function(){var e=void 0!==DTM.config.mrf_enabled?DTM.config.mrf_enabled:DTM.tools.allowAll;(!e||_satellite.getVar("platform")!=DTM.PLATFORM.AMP&&_satellite.getVar("platform")!=DTM.PLATFORM.WIDGET||(e=!1),e)&&(e=-1==["autor","buscador","concursos","desconocido","diarioas","ecuador#","formularios","promocionespapel","republica-dominicana","scripts","player"].indexOf(_satellite.getVar("primaryCategory")));return e=e?DTM.tools.ENABLED:DTM.tools.DISABLED },ABTesting:function(){if(_satellite.getVar("platform")==DTM.PLATFORM.FBIA)return!1;if("portada"!=_satellite.getVar("pageType")&&"portadilla"!=_satellite.getVar("pageType")&&"articulo"!=_satellite.getVar("pageType"))return!1;var e=document.createElement("script");e.setAttribute("language","javascript"),e.setAttribute("type","module"),e.setAttribute("src",DTM.tools.marfeel.lib.testab("module")),document.head.appendChild(e);var t=document.createElement("script");t.setAttribute("language","javascript"),t.setAttribute("type","text/javascript"),t.setAttribute("nomodule",""),t.setAttribute("src",DTM.tools.marfeel.lib.testab("nomodule")),document.head.appendChild(t)},utils:{mediaTimeFunction:function(e){void 0!==DTM.tools.marfeel.dl.mediaControls[e]&&(DTM.tools.marfeel.dl.mediaControls[e].currentTime+=5,window.marfeel.cmd.push(["multimedia",function(t){t.registerEvent(e,"updateCurrentTime",DTM.tools.marfeel.dl.mediaControls[e].currentTime)}]))},markTimeLoads:function(e){"object"!=typeof window.targetTimeLoad&&(window.targetTimeLoad={}),"object"!=typeof window.targetTimeLoad.markedEvents&&(window.targetTimeLoad.markedEvents={}),void 0===window.targetTimeLoad.markedEvents[e]&&(window.targetTimeLoad[e]=performance.now(),window.targetTimeLoad.markedEvents[e]=!0),Object.keys(targetTimeLoad).length>=26&&!window.targetTimeLoad.isAllMarkedEvents&&(window.marfeel=window.marfeel||{cmd:[]},window.marfeel.cmd.push(["compass",function(e){for(let t in window.targetTimeLoad)e.setPageVar(t,window.targetTimeLoad[t]);e.trackConversion("MarkTimeLoad"),window.targetTimeLoad.isAllMarkedEvents=!0}]))},mediaIntervals:function(e,t,a){if("set"==t){if(void 0===DTM.tools.marfeel.dl.mediaControls[e]){DTM.tools.marfeel.dl.mediaControls[e]={};var r={intervalo:setInterval((function(){DTM.tools.marfeel.utils.mediaTimeFunction(e)}),5e3),currentTime:a};DTM.tools.marfeel.dl.mediaControls[e]=r}}else"clear"==t&&(clearInterval(DTM.tools.marfeel.dl.mediaControls[e].intervalo),delete DTM.tools.marfeel.dl.mediaControls[e])}}},comscore:{enabled:1,dl:{},consents:-1,consentsID:77,map:{consents:{}},trackedPV:!1,init:function(){DTM.utils.isUE()?(window.didomiOnReady=window.didomiOnReady||[],window.didomiOnReady.push((function(){Didomi.getUserStatus().vendors.consent.enabled.indexOf(77)>-1&&(DTM.tools.comscore.enabled=DTM.tools.comscore.isEnabled(),DTM.tools.comscore.consents=DTM.CONSENTS.DEFAULT,DTM.tools.comscore.enabled!=DTM.tools.DISABLED&&DTM.tools.list.push("comscore"),DTM.tools.comscore.createMap(),DTM.tools.comscore.setDL({id:"production"==_satellite.environment.stage&&_satellite.getVar("validPage")?"8671776":"-1",pbn:"PRISA",src:"1"==_satellite.getVar("ssl")?"https://sb.scorecardresearch.com":"http://b.scorecardresearch.com",c3:encodeURIComponent("ELPAIS.COM Sites"),c4:encodeURIComponent("ELPAIS.COM"),img:new Image(1,1)}),DTM.tools.comscore.enabled!=DTM.tools.DISABLED&&!1!==_satellite.getVar("videoContent")&&(DTM.tools.comscore.videoMetrix.enabled=!0,DTM.tools.comscore.videoMetrix.load())),window.didomiEventListeners=window.didomiEventListeners||[],window.didomiEventListeners.push({event:"consent.changed",listener:function(){Didomi.getUserStatus().vendors.consent.enabled.indexOf(77)>-1&&(DTM.tools.comscore.enabled=DTM.tools.comscore.isEnabled(),DTM.tools.comscore.consents=DTM.CONSENTS.DEFAULT,DTM.tools.comscore.enabled!=DTM.tools.DISABLED&&DTM.tools.list.push("comscore"),DTM.tools.comscore.createMap(),DTM.tools.comscore.setDL({id:"production"==_satellite.environment.stage&&_satellite.getVar("validPage")?"8671776":"-1",pbn:"PRISA",src:"1"==_satellite.getVar("ssl")?"https://sb.scorecardresearch.com":"http://b.scorecardresearch.com",c3:encodeURIComponent("ELPAIS.COM Sites"),c4:encodeURIComponent("ELPAIS.COM"),img:new Image(1,1)}),DTM.tools.comscore.enabled!=DTM.tools.DISABLED&&!1!==_satellite.getVar("videoContent")&&(DTM.tools.comscore.videoMetrix.enabled=!0,DTM.tools.comscore.videoMetrix.load()),DTM.tools.comscore.trackPV())}})}))):(DTM.tools.comscore.enabled=DTM.tools.comscore.isEnabled(),DTM.tools.comscore.consents=DTM.CONSENTS.DEFAULT,DTM.tools.comscore.enabled!=DTM.tools.DISABLED&&DTM.tools.list.push("comscore"),DTM.tools.comscore.createMap(),DTM.tools.comscore.setDL({id:"production"==_satellite.environment.stage&&_satellite.getVar("validPage")?"8671776":"-1",pbn:"PRISA",src:"1"==_satellite.getVar("ssl")?"https://sb.scorecardresearch.com":"http://b.scorecardresearch.com",c3:encodeURIComponent("ELPAIS.COM Sites"),c4:encodeURIComponent("ELPAIS.COM"),img:new Image(1,1)}),DTM.tools.comscore.enabled!=DTM.tools.DISABLED&&!1!==_satellite.getVar("videoContent")&&(DTM.tools.comscore.videoMetrix.enabled=!0,DTM.tools.comscore.videoMetrix.load()),DTM.tools.comscore.trackPV())},getDL:function(){return this.dl},setDL:function(e){this.dl=e},isEnabled:function(){var e=void 0!==DTM.config.csc_enabled?DTM.config.csc_enabled:DTM.tools.allowAll;return!e||_satellite.getVar("platform")!=DTM.PLATFORM.FBIA&&_satellite.getVar("platform")!=DTM.PLATFORM.WIDGET||(e=!1),e&&"brasil.elpais.com"==_satellite.getVar("server")&&(e=!1),e=e?DTM.tools.ENABLED:DTM.tools.DISABLED},createMap:function(){this.map.consents[DTM.CONSENTS.WAITING]="",this.map.consents[DTM.CONSENTS.DEFAULT]="1",this.map.consents[DTM.CONSENTS.ACCEPT]="1",this.map.consents[DTM.CONSENTS.REJECT]="0"},trackPV:function(){if(this.enabled!=DTM.tools.ENABLED||!0===this.trackedPV)return!1;if(this.consents==DTM.CONSENTS.WAITING)return!1;this.getDL();window._comscore=window._comscore||[],window._comscore.push({c1:"2",c2:"8671776",options:{enableFirstPartyCookie:!0},cs_ucfr:this.map.consents[this.consents]}),function(){var e=document.createElement("script"),t=document.getElementsByTagName("script")[0];e.async=!0,e.src="https://sb.scorecardresearch.com/cs/8671776/beacon.js",t.parentNode.insertBefore(e,t)}(),this.trackedPV=!0},trackAsyncPV:function(){if(this.enabled!=DTM.tools.ENABLED)return!1;this.getDL();"undefined"!=typeof COMSCORE&&COMSCORE.beacon({c1:"2",c2:"8671776",options:{enableFirstPartyCookie:!0},cs_ucfr:this.map.consents[this.consents]})},trackEvent:function(e){if(this.enabled==DTM.tools.DISABLED)return DTM.events.setEffect(e,"comscore",!1),!1;this.getDL();var t=!1;if(void 0===_satellite.getVar("event")[e])return DTM.notify("ComScore event past not valid <"+a+">","error"),!1;var a=_satellite.getVar("event")[e].eventInfo.eventName,r=_satellite.getVar("event")[e].attributes,i=r.hasOwnProperty("currentTime")?1e3*r.currentTime:-1,s=r.hasOwnProperty("mediaID")?r.mediaID:!!r.hasOwnProperty("videoID")&&r.videoID,n=r.hasOwnProperty("playerType")?DTM.utils.getPlayerType(r.playerType):"";switch(a){case"photogallery":"undefined"!=typeof COMSCORE&&(COMSCORE.beacon({c1:"2",c2:"8671776",options:{enableFirstPartyCookie:!0},cs_ucfr:this.map.consents[this.consents]}),t=!0);break;case DTM.events.VIDEOREADY:t=!(!1===this.videoMetrix.enabled||!this.videoMetrix.isValidPlayer(n)||!1===s||!this.videoMetrix.init(s));break;case DTM.events.VIDEORELOAD:!1!==this.videoMetrix.enabled&&this.videoMetrix.isValidPlayer(n)&&!1!==s?(this.videoMetrix.replay(s),t=!0):t=!1;break;case DTM.events.ADPLAY:case DTM.events.ADRESUMED:case DTM.events.VIDEOPLAY:case DTM.events.VIDEORESUMED:!1!==this.videoMetrix.enabled&&this.videoMetrix.isValidPlayer(n)&&!1!==s&&this.videoMetrix.init(s)?(a==DTM.events.ADPLAY||a==DTM.events.ADRESUMED?this.videoMetrix.setAdMetadata(r,s):this.videoMetrix.setMetadata(r,s),this.videoMetrix.play(s,a,i),t=!0):t=!1;break;case DTM.events.VIDEOEND:case DTM.events.ADEND:case DTM.events.ADSKIP:!1!==this.videoMetrix.enabled&&this.videoMetrix.isValidPlayer(n)&&!1!==s&&this.videoMetrix.init(s)?(this.videoMetrix.end(s,a,i),t=!0):t=!1;break;case DTM.events.VIDEOPAUSED:case DTM.events.ADPAUSED:!1!==this.videoMetrix.enabled&&this.videoMetrix.isValidPlayer(n)&&!1!==s&&this.videoMetrix.init(s)?(this.videoMetrix.pause(s,a,i),t=!0):t=!1;break;default:t=!1}return t&&DTM.notify("Event <"+a+"> tracked in tool <ComScore>"),DTM.events.setEffect(e,"comscore",t),t},videoMetrix:{enabled:!1,initialized:!1,myStreamingAnalytics:[],lib:"https://ep00.epimg.net/js/comun/streamsense.js",load:function(){var e=DTM.tools.comscore.dl;DTM.utils.loadScript(this.lib,(function(){window.ns_=ns_.analytics,window.ns_.PlatformApi.setPlatformAPI(window.ns_.PlatformApi.PlatformApis.WebBrowser),window.ns_.configuration.addClient(new window.ns_.configuration.PublisherConfiguration({publisherId:e.id})),window.ns_.configuration.setUsagePropertiesAutoUpdateMode(window.ns_.configuration.UsagePropertiesAutoUpdateMode.FOREGROUND_AND_BACKGROUND)}))},init:function(e){return!1!==this.enabled&&void 0!==window.ns_&&void 0!==e&&(this.initialized||(this.initialized=!0,window.ns_.start()),void 0===this.myStreamingAnalytics[e]&&(this.myStreamingAnalytics[e]={sa:new window.ns_.StreamingAnalytics,state:"",currentTime:0},this.myStreamingAnalytics[e].sa.createPlaybackSession()),!0)},isValidPlayer:function(e){return-1==["youtube"].indexOf(e)},setMetadata:function(e,t){if(void 0===window.ns_||void 0===e||!1===t)return!1;var a=DTM.tools.comscore.dl,r=e.hasOwnProperty("mediaRepType")?e.mediaRepType:e.hasOwnProperty("videoRepType")?e.videoRepType:"";r=""!=r?"streaming"==r?window.ns_.StreamingAnalytics.ContentMetadata.ContentType.LIVE:window.ns_.StreamingAnalytics.ContentMetadata.ContentType.SHORT_FORM_ON_DEMAND:"";var i=e.hasOwnProperty("mediaDuration")?e.mediaDuration:e.hasOwnProperty("videoDuration")?e.videoDuration:"";i=""!=i?1e3*parseInt(i):0;var s=new ns_.StreamingAnalytics.ContentMetadata;s.setMediaType(r),s.setUniqueId(!1===t?"null":t),s.setLength(i),s.setDictionaryClassificationC3(a.c3),s.setDictionaryClassificationC4(a.c4),s.setDictionaryClassificationC6("*null"),s.setPublisherName(a.pbn),this.myStreamingAnalytics[t].sa.setMetadata(s)},setAdMetadata:function(e,t){if(void 0===window.ns_||void 0===e||!1===t)return!1;var a=DTM.tools.comscore.dl,r=e.hasOwnProperty("mediaRepType")?e.mediaRepType:e.hasOwnProperty("videoRepType")?e.videoRepType:"";r=""!=r?"streaming"==r?window.ns_.StreamingAnalytics.ContentMetadata.ContentType.LIVE:window.ns_.StreamingAnalytics.ContentMetadata.ContentType.SHORT_FORM_ON_DEMAND:"";var i=e.hasOwnProperty("mediaDuration")?e.mediaDuration:e.hasOwnProperty("videoDuration")?e.videoDuration:"";i=""!=i?1e3*parseInt(i):0;var s=new ns_.StreamingAnalytics.ContentMetadata;s.setMediaType(r),s.setUniqueId(!1===t?"null":t),s.setLength(i),s.setDictionaryClassificationC3(a.c3),s.setDictionaryClassificationC4(a.c4),s.setDictionaryClassificationC6("*null"),s.setPublisherName(a.pbn);var n=new window.ns_.StreamingAnalytics.AdvertisementMetadata,o="";if(void 0!==e.adMode)switch(e.adMode){case"post-roll":case"postroll":o=window.ns_.StreamingAnalytics.AdvertisementMetadata.AdvertisementType.ON_DEMAND_POST_ROLL;break;case"pre-roll":case"preroll":o=window.ns_.StreamingAnalytics.AdvertisementMetadata.AdvertisementType.ON_DEMAND_PRE_ROLL;break;case"mid-roll":case"midroll":o=window.ns_.StreamingAnalytics.AdvertisementMetadata.AdvertisementType.ON_DEMAND_MID_ROLL}n.setMediaType(o),n.setRelatedContentMetadata(s),this.myStreamingAnalytics[t].sa.setMetadata(n)},play:function(e,t,a){if(void 0===window.ns_||void 0===e)return!1;t==DTM.events.VIDEORESUMED&&this.myStreamingAnalytics[e].state===DTM.events.VIDEOPAUSED&&a!=this.myStreamingAnalytics[e].currentTime?(this.myStreamingAnalytics[e].sa.startFromPosition(a),this.myStreamingAnalytics[e].sa.notifySeekStart()):this.myStreamingAnalytics[e].sa.notifyPlay(),this.myStreamingAnalytics[e].state=t,this.myStreamingAnalytics[e].currentTime=a},replay:function(e){if(void 0===window.ns_||void 0===e)return!1;void 0!==this.myStreamingAnalytics[e]&&delete this.myStreamingAnalytics[e]},pause:function(e,t,a){if(void 0===window.ns_||void 0===e)return!1;this.myStreamingAnalytics[e].sa.notifyPause(),this.myStreamingAnalytics[e].state=t,this.myStreamingAnalytics[e].currentTime=a},end:function(e,t,a){if(void 0===window.ns_||void 0===e)return!1;this.myStreamingAnalytics[e].sa.notifyEnd(),this.myStreamingAnalytics[e].state=t,this.myStreamingAnalytics[e].currentTime=a}}},facebook:{enabled:1,dl:{},consents:-1,consentsID:"c:facebook-YyJRAyed",trackedPV:!1,init:function(){this.enabled=this.isEnabled(),this.consents=DTM.CONSENTS.DEFAULT,this.enabled!=DTM.tools.DISABLED&&DTM.tools.list.push("facebook"),this.setDL({id:"1461658713846525",idHavas:"807598982615379",src:"https://www.facebook.com/tr",trackingCode:""!=_satellite.getVar("campaign")?_satellite.getVar("campaign"):"none",campaign:""!=_satellite.getVar("campaign")?_satellite.getVar("campaign"):"none"})},getDL:function(){return this.dl},setDL:function(e){this.dl=e},isEnabled:function(){var e=void 0!==DTM.config.fbk_enabled?DTM.config.fbk_enabled:DTM.tools.allowAll;return e&&_satellite.getVar("platform")==DTM.PLATFORM.WIDGET&&(e=!1),e=(e=e&&!0===_satellite.getVar("validPage")&&!1===_satellite.getVar("translatePage"))?DTM.tools.ENABLED:DTM.tools.DISABLED},trackPV:function(e){if("undefined"!=typeof Didomi&&void 0!==Didomi.getUserConsentStatusForVendor&&Didomi.getUserConsentStatusForVendor("c:facebook-YyJRAyed")&&(this.consents=1),this.enabled!=DTM.tools.ENABLED||void 0===e&&this.trackedPV||_satellite.getVar("platform")!=DTM.PLATFORM.FBIA&&this.consents!==DTM.CONSENTS.ACCEPT)return!1;var t=this.getDL();DTM.utils.sendBeacon(t.src,{id:t.id,ev:"PageView",dl:_satellite.getVar("destinationURL"),rl:_satellite.getVar("referringURL")},!1,"ts"),DTM.utils.sendBeacon(t.src,{id:t.id,ev:"ViewContent",dl:_satellite.getVar("destinationURL"),rl:_satellite.getVar("referringURL"),"cd[campaign]":t.campaign,"cd[content_name]":_satellite.getVar("pageName"),"cd[content_category]":_satellite.getVar("primaryCategory"),"cd[registeredUser]":"1"==_satellite.getVar("user:registeredUser")?"reg":"anon","cd[sysEnv]":_satellite.getVar("sysEnv"),"cd[trackingCode]":t.trackingCode,"cd[userType]":_satellite.getVar("user:type"),"cd[paywallBlock]":"bloqueante"==_satellite.getVar("paywall:contentAdType")?"1":"0"},!1,"ts"),"epmas>suscripcion>confirmation"==_satellite.getVar("subCategory2")&&DTM.utils.sendBeacon(t.src,{id:t.id,ev:"SubsComplete",dl:_satellite.getVar("destinationURL"),rl:_satellite.getVar("referringURL"),"cd[content_name]":_satellite.getVar("pageName"),"cd[content_category]":_satellite.getVar("primaryCategory"),"cd[sysEnv]":_satellite.getVar("sysEnv"),"cd[sku]":_satellite.getVar("paywall:cartProduct"),"cd[userType]":_satellite.getVar("user:type")},!1,"ts");var a={"epmas>suscripcion>checkout":"InitiateCheckout","epmas>suscripcion>payment":"AddPaymentInfo","epmas>suscripcion>confirmation":"Purchase"};a.hasOwnProperty(_satellite.getVar("subCategory2"))&&DTM.utils.sendBeacon(t.src,{id:t.idHavas,ev:a[_satellite.getVar("subCategory2")],dl:_satellite.getVar("destinationURL"),rl:_satellite.getVar("referringURL")},!1,"ts"),DTM.utils.sendBeacon(t.src,{id:t.idHavas,ev:"PageView",dl:_satellite.getVar("destinationURL"),rl:_satellite.getVar("referringURL")},!1,"ts"),this.trackedPV=!0},trackAsyncPV:function(){this.trackPV(!0)},trackEvent:function(e){if(this.enabled==DTM.tools.DISABLED||this.consents!==DTM.CONSENTS.ACCEPT)return DTM.events.setEffect(e,"facebook",!0),!1;var t=this.getDL(),a=!1;if(void 0===_satellite.getVar("event")[e])return DTM.notify("Facebook event past not valid <"+r+">","error"),!1;var r=_satellite.getVar("event")[e].eventInfo.eventName,i=_satellite.getVar("event")[e].attributes;return r==DTM.events.UUVINC||r==DTM.events.USERREGISTER?(DTM.utils.sendBeacon(t.src,{id:t.id,ev:"CompleteRegistration",dl:_satellite.getVar("destinationURL"),rl:_satellite.getVar("referringURL"),"cd[campaign]":t.campaign,"cd[content_name]":_satellite.getVar("pageName"),"cd[content_category]":_satellite.getVar("primaryCategory"),"cd[registeredUser]":"1"==_satellite.getVar("user:registeredUser")?"reg":"anon","cd[sysEnv]":_satellite.getVar("sysEnv"),"cd[trackingCode]":t.trackingCode,"cd[userType]":_satellite.getVar("user:type"),"cd[status]":r==DTM.events.USERREGISTER?"register":"vinculation","cd[reg_origin]":void 0!==i.registerOrigin?i.registerOrigin:"","cd[reg_prod_origin]":void 0!==i.registerProd?i.registerProd:"","cd[reg_type]":r==DTM.events.UUVINC?"vinculation":"undefined"!=i.registerType?"clasico"==i.registerType?"classic":"social("+i.registerType+")":""},!1,"ts"),a=!0):r==DTM.events.CHECKOUT&&(DTM.utils.sendBeacon(t.src,{id:t.id,ev:"InitiateCheckout",dl:_satellite.getVar("destinationURL"),rl:_satellite.getVar("referringURL")},!1,"ts"),a=!0),a&&DTM.notify("Event <"+r+"> tracked in tool <Facebook>"),DTM.events.setEffect(e,"facebook",a),a}},elpais:{enabled:1,dl:{},trackedPV:!1,eventQueue:[],map:{events:{},vars:{}},init:function(){this.enabled=this.isEnabled(),this.enabled!=DTM.tools.DISABLED&&DTM.tools.list.push("elpais"),this.createMap(),this.setDL({img:null,src:{realTime:("production"==_satellite.environment.stage&&_satellite.getVar("validPage"),""),pep:"//pxlctl.elpais.com/pxlctl.gif",cloudfront:"//d30wo2lffetbp8.cloudfront.net/"},realTime:{piid:"not-set",pn:"not-set",g:"not-set",ch:"not-set",tit:"not-set",typ:"not-set",h:"not-set",r:"not-set",cms:"not-set",edn:"not-set",edc:"not-set",ts:"not-set",co:"not-set",sys:"not-set",uid:"not-set",arcid:"not-set",aid:"not-set",ust:"not-set",ustamp:"not-set",usty:"not-set",pwt:"not-set",pws:"not-set",pwp:"not-set",pwcart:"not-set",pwstep:"not-set",pwact:"not-set",pwcou:"not-set",pwad:"not-set",pwori:"not-set",pwmod:"not-set",pwtrty:"not-set"}})},createMap:function(){this.map.events[DTM.events.PHOTOGALLERY]="photogallery",this.map.events[DTM.events.SCROLLINF]="scrollInf",this.map.events[DTM.events.RECOMMENDERIMPRESSION]="r",this.map.events[DTM.events.INTERNALPIXEL]="internalPixel",this.map.events[DTM.events.USERREGISTER]="okreg",this.map.events[DTM.events.USERLOGIN]="oklog",this.map.events[DTM.events.READARTICLE]="readArticle",this.map.events[DTM.events.VIDEOPLAY]="videoPlay",this.map.events[DTM.events.VIDEO25]="video25",this.map.events[DTM.events.VIDEO50]="video50",this.map.events[DTM.events.VIDEO75]="video75",this.map.events[DTM.events.VIDEOEND]="videoEnd",this.map.events[DTM.events.CHECKOUT]="checkout",this.map.vars.recommenderTime1="t1",this.map.vars.recommenderTime="t",this.map.vars.recommenderError="e",this.map.vars.recommenderTo="to",this.map.vars.recommenderS="s",this.map.vars.userID="u",this.map.vars.registerType="rgt",this.map.vars.registerOrigin="rgo",this.map.vars.registerProd="rgp",this.map.vars.videoName="vn",this.map.vars.mediaName="vn",this.map.vars.registerBackURL="rbu",this.map.vars.paywallTransactionType="pwtrty"},getDL:function(){return this.dl},setDL:function(e){this.dl=e},isEnabled:function(){var e=void 0!==DTM.config.ep_enabled?DTM.config.ep_enabled:DTM.tools.allowAll;return e&&_satellite.getVar("platform")==DTM.PLATFORM.WIDGET&&(e=!1),e=e?DTM.tools.ENABLED:DTM.tools.DISABLED},trackPV:function(e){if(this.enabled!=DTM.tools.ENABLED||void 0===e&&this.trackedPV)return!1;var t=this.getDL();t.realTime.piid=_satellite.getVar("pageInstanceID"),t.realTime.pn=_satellite.getVar("pageName"),t.realTime.g=_satellite.getVar("destinationURL"),t.realTime.ch=_satellite.getVar("primaryCategory"),t.realTime.tit=_satellite.getVar("pageTitle"),t.realTime.typ=_satellite.getVar("pageType"),t.realTime.h=_satellite.getVar("server"),t.realTime.r=_satellite.getVar("referringURL"),t.realTime.edn=_satellite.getVar("editionNavigation"),t.realTime.edc=_satellite.getVar("edition"),t.realTime.cms=_satellite.getVar("cms"),t.realTime.sys=_satellite.getVar("sysEnv"),t.realTime.ts=this.getTimeStamp(),t.realTime.aid=_satellite.getVar("user:experienceCloudID"),t.realTime.uid=_satellite.getVar("user:profileID"),t.realTime.arcid=_satellite.getVar("user:ID"),t.realTime.co=_satellite.getVar("user:country"),t.realTime.ust=_satellite.getVar("user:registeredUser"),t.realTime.ustamp=_satellite.getVar("user:registeredUserAMP"),t.realTime.usty=_satellite.getVar("user:type"),t.realTime.pwt=_satellite.getVar("paywall:signwallType"),t.realTime.pws="1"==_satellite.getVar("paywall:contentBlocked")?"cerrado":"abierto",t.realTime.pwp=_satellite.getVar("user:subscriptions"),t.realTime.pwstep=this.getPaywallStep(),t.realTime.pwact=!0===_satellite.getVar("paywall:active")?"activo":!1===_satellite.getVar("paywall:active")?"inactivo":"not-set",t.realTime.pwcou=_satellite.getVar("paywall:counter"),t.realTime.pwad=_satellite.getVar("paywall:contentAdType"),t.realTime.pwcart="not-set"!=_satellite.getVar("paywall:cartProduct")?_satellite.getVar("paywall:cartProduct"):"",t.realTime.pwori=_satellite.getVar("paywall:transactionOrigin"),t.realTime.pwmod=_satellite.getVar("paywall:type"),t.realTime.pwtrty=_satellite.getVar("paywall:transactionType");var a=DTM.utils.copyObject(t.realTime);for(var r in a.ev="pageView",this.trackedPV=!1,this.eventQueue)this.trackEvent(r)},trackAsyncPV:function(){this.trackPV(!0)},trackEvent:function(e){if(this.enabled==DTM.tools.DISABLED)return DTM.events.setEffect(e,"elpais",!1),!1;if(void 0===_satellite.getVar("event")[e])return DTM.notify("EL PAIS event past not valid <"+t+">","error"),!1;var t=_satellite.getVar("event")[e].eventInfo.eventName,a=_satellite.getVar("event")[e].attributes,r=this.map.events[t];if(!this.map.events.hasOwnProperty(t))return DTM.events.setEffect(e,"elpais",!1),!1;if(this.isEnabled==DTM.tools.ENABLED&&!this.trackedPV)return this.eventQueue.push(e),DTM.events.setEffect(e,"elpais",!1),!1;var i=this.getDL(),s=!1;switch(t){case DTM.events.USERREGISTER:case DTM.events.USERLOGIN:case DTM.events.READARTICLE:case DTM.events.CHECKOUT:i.realTime.ts=this.getTimeStamp(),t==DTM.events.CHECKOUT&&(i.realTime.pwstep="checkout",i.realTime.pwcart=void 0!==a.paywallCartProduct?a.paywallCartProduct:"not-set"!=_satellite.getVar("paywall:cartProduct")?_satellite.getVar("paywall:cartProduct"):"");var n=DTM.utils.copyObject(i.realTime);for(var o in n.ev=r,this.map.vars)a.hasOwnProperty(o)&&(n[this.map.vars[o]]=a[o]);s=!1;break;case DTM.events.INTERNALPIXEL:case DTM.events.RECOMMENDERIMPRESSION:if((n=[]).ch=_satellite.getVar("primaryCategory"),a.hasOwnProperty("userID")||(a.userID=_satellite.getVar("user:profileID")),"object"==typeof a.extraParams)for(var l in a.extraParams)n[l]=a.extraParams[l];for(var o in this.map.vars)a.hasOwnProperty(o)&&(n[this.map.vars[o]]="e"==this.map.vars[o]?a[o].toUpperCase():a[o]);r=a.hasOwnProperty("pixelName")?a.pixelName:"r";s=DTM.utils.sendBeacon(i.src.cloudfront+encodeURIComponent(r)+".gif",n,!1,!1,!1);break;default:s=!1}return s&&DTM.notify("Event <"+t+"> tracked in tool <EL PAIS>"),DTM.events.setEffect(e,"elpais",s),s},getTimeStamp:function(e){var t="";if(e)t=_satellite.getVar("date:fullYear")+"/"+_satellite.getVar("date:month")+"/"+_satellite.getVar("date:day")+"T"+_satellite.getVar("date:hours")+":"+_satellite.getVar("date:minutes")+":"+_satellite.getVar("date:seconds");else{var a=new Date;t=a.getFullYear()+"/"+DTM.utils.formatDate(a.getMonth()+1)+"/"+DTM.utils.formatDate(a.getDate())+"T"+DTM.utils.formatDate(a.getHours())+":"+DTM.utils.formatDate(a.getMinutes())+":"+DTM.utils.formatDate(a.getSeconds())}return t},getPaywallStep:function(){var e="";if("epmas"==_satellite.getVar("primaryCategory"))switch(_satellite.getVar("subCategory2")){case"epmas>suscripcion>home":e="landing";break;case"epmas>suscripcion>registro":-1==_satellite.getVar("referringURL").indexOf("elpais.com/landing_oferta")&&-1==document.referrer.indexOf("elpais.com/landing_oferta")&&-1==_satellite.getVar("referringURL").indexOf("elpais.com/suscripciones")&&-1==document.referrer.indexOf("elpais.com/suscripciones")||(e="registro");break;case"epmas>suscripcion>login":-1==_satellite.getVar("referringURL").indexOf("elpais.com/landing_oferta")&&-1==document.referrer.indexOf("elpais.com/landing_oferta")&&-1==_satellite.getVar("referringURL").indexOf("elpais.com/suscripciones")&&-1==document.referrer.indexOf("elpais.com/suscripciones")||(e="login");break;case"epmas>suscripcion>checkout":e="checkout";break;case"epmas>suscripcion>payment":e="payment";break;case"epmas>suscripcion>confirmation":e=""!=_satellite.getVar("paywall:transactionID")?"confirmation":"";break;default:-1!=_satellite.getVar("pageName").indexOf("elpaiscom/suscripciones/oferta/")&&(e="")}return e}},google:{enabled:!0,dl:{},trackedPV:!1,consents:-1,consentsID:"google",init:function(){if("undefined"!=typeof Didomi&&Didomi.getUserConsentStatusForVendor("google")){this.enabled=this.isEnabled(),this.enabled!=DTM.tools.DISABLED&&DTM.tools.list.push("google"),this.consents=DTM.CONSENTS.DEFAULT,this.setDL({ep:"//googleads.g.doubleclick.net/pagead/viewthroughconversion/",pbs:"https://pubads.g.doubleclick.net/activity;",floodlight:"https://ad.doubleclick.net/ddm/activity"});var e=document.createElement("script");e.async=!0,e.src="https://www.googletagmanager.com/gtag/js?id=AW-10850525560",document.querySelector("head").appendChild(e)}},getDL:function(){return this.dl},setDL:function(e){this.dl=e},isEnabled:function(){var e=void 0!==DTM.config.goo_enabled?DTM.config.goo_enabled:DTM.tools.allowAll;return!e||_satellite.getVar("platform")!=DTM.PLATFORM.FBIA&&_satellite.getVar("platform")!=DTM.PLATFORM.WIDGET||(e=!1),e=e?DTM.tools.ENABLED:DTM.tools.DISABLED},trackPV:function(){if(this.enabled!=DTM.tools.ENABLED||this.consents!==DTM.CONSENTS.ACCEPT)return!1;var e=this.getDL();if(DTM.utils.sendBeacon(e.ep+"965296472/",{value:"0",guid:"ON",script:"0"},!1,"rnd"),"mx"==_satellite.getVar("user:country")&&DTM.utils.sendBeacon(e.ep+"802913665/",{value:"0",guid:"ON",script:"0"},!1,"rnd"),"epmas"==_satellite.getVar("primaryCategory"))switch(_satellite.getVar("subCategory2")){case"epmas>suscripcion>home":DTM.utils.sendBeacon(e.floodlight+"/src=8310699;type=visit_ep;cat=lpg_s0;u9="+_satellite.getVar("server")+";dc_lat=;dc_rdid=;tag_for_child_directed_treatment=;tfua=;npa=;gdpr=${GDPR};gdpr_consent=${GDPR_CONSENT_755};ord="+1e13*Math.random()+"?",{},!1);break;case"epmas>suscripcion>checkout":DTM.utils.sendBeacon(e.floodlight+"/src=8310699;type=visit_ep;cat=cnv_s0;u9="+_satellite.getVar("server")+";dc_lat=;dc_rdid=;tag_for_child_directed_treatment=;tfua=;npa=;gdpr=${GDPR};gdpr_consent=${GDPR_CONSENT_755};ord="+1e13*Math.random()+"?",{},!1),DTM.utils.sendBeacon(e.pbs+"xsp=4617931;ord="+1e13*Math.random()+"?",{},!1);break;case"epmas>suscripcion>payment":DTM.utils.sendBeacon(e.floodlight+"/src=8310699;type=visit_ep;cat=cnv_s00u2="+_satellite.getVar("user:subscriptions")+";u9="+_satellite.getVar("server")+";dc_lat=;dc_rdid=;tag_for_child_directed_treatment=;tfua=;npa=;gdpr=${GDPR};gdpr_consent=${GDPR_CONSENT_755};ord="+1e13*Math.random()+"?",{},!1);break;case"epmas>suscripcion>confirmation":DTM.utils.sendBeacon(e.floodlight+"/src=8310699;type=sales;cat=cnv_s0;qty=1;cost=[Revenue];u2="+_satellite.getVar("user:subscriptions")+";u9="+_satellite.getVar("server")+";dc_lat=;dc_rdid=;tag_for_child_directed_treatment=;tfua=;npa=;gdpr=${GDPR};gdpr_consent=${GDPR_CONSENT_755};ord="+_satellite.getVar("paywall:transactionID")+"?",{},!1),DTM.utils.sendBeacon(e.pbs+"xsp=4623404;ord="+1e13*Math.random()+"?",{},!1)}if(document.location.href.indexOf("captacion-especial-5")>-1){function t(){dataLayer.push(arguments)}window.dataLayer=window.dataLayer||[],t("js",new Date),t("config","AW-10850525560")}document.location.href.indexOf("captacion-especial-5/#/confirmation")>-1&&t("event","conversion",{send_to:"AW-10850525560/vKSmCNbopvMZEPjC97Uo",value:18,currency:"EUR"}),this.trackedPV=!0},trackEvent:function(e){if(this.enabled!=DTM.tools.ENABLED||this.consents!==DTM.CONSENTS.ACCEPT)return DTM.events.setEffect(e,"google",!1),!1;var t=this.getDL(),a=!1;if(void 0===_satellite.getVar("event")[e])return DTM.notify("Google event past not valid <"+r+">","error"),!1;var r=_satellite.getVar("event")[e].eventInfo.eventName;_satellite.getVar("event")[e].attributes;return r==DTM.events.CHECKOUT&&(DTM.utils.sendBeacon(t.floodlight+"/src=8310699;type=visit_ep;cat=cnv_s0;u9="+_satellite.getVar("server")+";dc_lat=;dc_rdid=;tag_for_child_directed_treatment=;tfua=;npa=;gdpr=${GDPR};gdpr_consent=${GDPR_CONSENT_755};ord="+1e13*Math.random(),{},!1),DTM.utils.sendBeacon(t.pbs+"xsp=4617931;ord="+1e13*Math.random(),{},!1),a=!0),a&&DTM.notify("Event <"+r+"> tracked in tool <Google>"),DTM.events.setEffect(e,"google",a),a},trackAsyncPV:function(){this.trackPV()}},triton:{enabled:1,dl:{stationID:693093},trackedPV:!1,init:function(){"object"!=typeof tdIdsync&&document.URL.indexOf("suscr")<0&&_satellite.getVar("subCategory1").indexOf("suscr")<0&&(window.didomiOnReady=window.didomiOnReady||[],window.didomiOnReady.push((function(e){if(void 0!==e){if(e.getUserStatus().vendors.consent.enabled.indexOf(239)>-1){window.mm_didomi_cs_t=e.getUserConsentStatusForVendor("239");var t=window.cmpConsentString,a=(window.mm_didomi_cs_t,e.isRegulationApplied("gdpr")?1:0),r=document.createElement("script");r.type="text/javascript",r.src="https://playerservices.live.streamtheworld.com/api/idsync.js?stationId="+DTM.tools.triton.dl.stationID+"&gdpr="+a+"&gdpr_consent="+t,r.onload=function(){"undefined"!=typeof mm_demo&&mm_demo&&console.log("%cCookie Sync loaded","font-weight:bold;color:orange")};var i=document.getElementsByTagName("script")[0];i.parentNode.insertBefore(r,i)}}else{window.didomiOnReady=window.didomiOnReady||[],window.didomiOnReady.push((function(e){e.getObservableOnUserConsentStatusForVendor("239").subscribe((function(t){if(void 0===t)window.mm_didomi_cs_t=!1;else if(!0===t){window.mm_didomi_cs_t=e.getUserConsentStatusForVendor("239");var a=window.cmpConsentString,r=(window.mm_didomi_cs_t,e.isRegulationApplied("gdpr")?1:0),i=document.createElement("script");i.type="text/javascript",i.src="https://playerservices.live.streamtheworld.com/api/idsync.js?stationId="+DTM.tools.triton.dl.stationID+"&gdpr="+r+"&gdpr_consent="+a,i.onload=function(){"undefined"!=typeof mm_demo&&mm_demo&&console.log("%cCookie Sync loaded","font-weight:bold;color:orange")};var s=document.getElementsByTagName("script")[0];s.parentNode.insertBefore(i,s)}else!1===t&&(window.mm_didomi_cs_t=!1)}))}))}})))}},AEPConsents:{enabled:!0,dl:{},trackedPV:!1,vendors_list:{"c:0anuncian-BzrcXrYe":"la_liga","c:anunciante_la_liga":"la_liga"},init:function(){this.enabled=this.isEnabled(),this.enabled!=DTM.tools.DISABLED&&DTM.tools.list.push("AEPConsents")},isEnabled:function(){var e=void 0!==DTM.config.consent_send_enabled?DTM.config.consent_send_enabled:DTM.tools.allowAll;return!e||_satellite.getVar("platform")!=DTM.PLATFORM.FBIA&&_satellite.getVar("platform")!=DTM.PLATFORM.WIDGET||(e=!1),e=e?DTM.tools.ENABLED:DTM.tools.DISABLED},trackPV:function(){if(this.enabled!=DTM.tools.ENABLED)return!1;window.didomiOnReady=window.didomiOnReady||[],window.didomiOnReady.push((function(e){function t(t){consentData=e.getUserStatus(),acceptedPurposses=consentData.purposes.consent.enabled,rejectedPurposses=consentData.purposes.consent.disabled,enabled_json={};for(const e of acceptedPurposses)switch(e){case"sharingda-aQwVWdxj":enabled_json.data_sharing_web="y";break;case"sharingof-wG7bxM8E":enabled_json.data_sharing="y";break;default:enabled_json[e]="y"}disabled_json={};for(const e of rejectedPurposses)switch(e){case"sharingda-aQwVWdxj":disabled_json.data_sharing_web="n";break;case"sharingof-wG7bxM8E":disabled_json.data_sharing="n";break;default:disabled_json[e]="n"}acceptedVendors=consentData.vendors.consent.enabled,rejectedVendors=consentData.vendors.consent.disabled,vendors_enabled_json={};for(const e of acceptedVendors)void 0!==DTM.tools.AEPConsents.vendors_list[e]&&(vendors_enabled_json[DTM.tools.AEPConsents.vendors_list[e]]="y");vendors_disabled_json={};for(const e of rejectedVendors)void 0!==DTM.tools.AEPConsents.vendors_list[e]&&(vendors_disabled_json[DTM.tools.AEPConsents.vendors_list[e]]="n");var a={};a="1"==digitalData.user.registeredUser&&""!=digitalData.user.profileID&&_satellite.getVar("user:experienceCloudID")?{ECID:[{id:_satellite.getVar("user:experienceCloudID"),primary:!1}],USUNUID:[{id:digitalData.user.profileID,primary:!0}]}:{ECID:[{id:_satellite.getVar("user:experienceCloudID"),primary:!0}]};var r=Object.assign(enabled_json,disabled_json),i=Object.assign(vendors_enabled_json,vendors_disabled_json);r.partners=i;var s="";"undefined"!=typeof didomiRemoteConfig&&void 0!==didomiRemoteConfig.notices[0]&&void 0!==didomiRemoteConfig.notices[0].notice_id&&(s="-"+didomiRemoteConfig.notices[0].notice_id);var n="pageview";t&&(n="consent update");var o={header:{schemaRef:{id:"https://ns.adobe.com/prisacom/schemas/8e2617119901b47918ccaf4d7e375a8be0842e54ba682af1",contentType:"application/vnd.adobe.xed-full+json;version=1"},imsOrgId:"2387401053DB208C0A490D4C@AdobeOrg",datasetId:"644125ae1894cf1c06549900",flowId:"766d9358-aa82-40f8-bf37-127e65cf06e1"},body:{xdmMeta:{schemaRef:{id:"https://ns.adobe.com/prisacom/schemas/8e2617119901b47918ccaf4d7e375a8be0842e54ba682af1",contentType:"application/vnd.adobe.xed-full+json;version=1"}},xdmEntity:{_prisacom:{consent:r}, identityMap:a,extSourceSystemAudit:{lastUpdatedBy:"didomi "+e.getTCFVersion()+s+"-"+_satellite.getVar("publisher").toLowerCase()+"-"+n,lastUpdatedDate:(new Date).toISOString()}}}};fetch("https://dcs.adobedc.net/collection/e571fc265fac50018a554f5329fd64e442c402492069befe67bd5410c95afea7",{method:"POST",body:JSON.stringify(o),headers:{"Content-Type":"application/json",Accept:"application/json"}}),DTM.tools.AEPConsents.trackedPV=!0}_satellite.getVar("user:experienceCloudID")&&38==_satellite.getVar("user:experienceCloudID").length&&new RegExp("^[0-9]+$").test(_satellite.getVar("user:experienceCloudID"))&&(e.shouldConsentBeCollected()?e.getObservableOnUserConsentStatusForVendor("565").subscribe((function(e){void 0===e||(!0===e||!1===e)&&t(!0)})):(window.didomiEventListeners=window.didomiEventListeners||[],window.didomiEventListeners.push({event:"consent.changed",listener:function(){t(!0)}}),t()))}))}},liveramp:{enabled:1,dl:{},consents:-1,consentsID:97,map:{consents:{}},trackedPV:!1,init:function(){this.enabled=this.isEnabled(),this.consents=DTM.CONSENTS.DEFAULT,this.enabled!=DTM.tools.DISABLED&&DTM.tools.list.push("liveramp"),this.createMap(),this.setDL({id:"a95fc332-885d-40c0-aa11-3c7c55aa0d7d"})},getDL:function(){return this.dl},setDL:function(e){this.dl=e},isEnabled:function(){var e=DTM.utils.getQueryParam("liveramp_enabled"),t=void 0!==DTM.config.liveramp_enabled?DTM.config.liveramp_enabled:"1"==e||"0"!=e&&DTM.tools.allowAll;return!t||_satellite.getVar("platform")!=DTM.PLATFORM.AMP&&_satellite.getVar("platform")!=DTM.PLATFORM.FBIA&&_satellite.getVar("platform")!=DTM.PLATFORM.WIDGET||(t=!1),t=t?DTM.tools.ENABLED:DTM.tools.DISABLED,_satellite.getVar("platform")==DTM.PLATFORM.AMPPLAYER&&(t=DTM.tools.ONLYEVENTS),t},createMap:function(){this.map.consents[DTM.CONSENTS.WAITING]="",this.map.consents[DTM.CONSENTS.DEFAULT]="1",this.map.consents[DTM.CONSENTS.ACCEPT]="1",this.map.consents[DTM.CONSENTS.REJECT]="0"},trackPV:function(){if(this.enabled!=DTM.tools.ENABLED||!0===this.trackedPV)return!1;if("undefined"==typeof ats){var e=this.getDL(),t=document.createElement("script"),a=document.getElementsByTagName("script")[0];t.setAttribute("defer",""),t.async=!0,t.src="https://ats-wrapper.privacymanager.io/ats-modules/"+e.id+"/ats.js",a.parentNode.insertBefore(t,a)}null!=DTM.utils.getCookie("hem")&&("undefined"==typeof ats?window.addEventListener("envelopeModuleReady",(()=>{atsenvelopemodule.setAdditionalData({type:"emailHashes",id:[DTM.utils.getCookie("hem")]})})):null!=DTM.utils.getCookie("hem")&&atsenvelopemodule.setAdditionalData({type:"emailHashes",id:[DTM.utils.getCookie("hem")]})),this.trackedPV=!0,DTM.notify("PV tracked in tool <LiveRamp> (Data Layer)")}},amazonaps:{enabled:1,dl:{src:"https://c.amazon-adsystem.com",path:"/aax2/apstag.js"},consents:-1,consentsID:394,map:{consents:{}},trackedPV:!1,init:function(){this.enabled=this.isEnabled(),this.consents=DTM.CONSENTS.DEFAULT,DTM.tools.list.push("amazonaps"),DTM.trackGDPRPV("amazonaps")},getDL:function(){return this.dl},setDL:function(e){this.dl=e},isEnabled:function(){var e=DTM.utils.getQueryParam("amzaps_enabled"),t=void 0!==DTM.config.amzaps_enabled?DTM.config.amzaps_enabled:"1"==e||"0"!=e&&DTM.tools.allowAll;return!t||_satellite.getVar("platform")!=DTM.PLATFORM.AMP&&_satellite.getVar("platform")!=DTM.PLATFORM.FBIA&&_satellite.getVar("platform")!=DTM.PLATFORM.WIDGET||(t=!1),t=t?DTM.tools.ENABLED:DTM.tools.DISABLED,_satellite.getVar("platform")==DTM.PLATFORM.AMPPLAYER&&(t=DTM.tools.ONLYEVENTS),t},createMap:function(){this.map.consents[DTM.CONSENTS.WAITING]="",this.map.consents[DTM.CONSENTS.DEFAULT]="1",this.map.consents[DTM.CONSENTS.ACCEPT]="1",this.map.consents[DTM.CONSENTS.REJECT]="0"},trackPV:function(){if(this.enabled!=DTM.tools.ENABLED||!0===this.trackedPV)return!1;try{if("undefined"==typeof apstag){!function(e,t){function a(a,r){t[e]._Q.push([a,r])}t[e]||(t[e]={init:function(){a("i",arguments)},fetchBids:function(){a("f",arguments)},setDisplayBids:function(){},targetingKeys:function(){return[]},dpa:function(){a("di",arguments)},rpa:function(){a("ri",arguments)},upa:function(){a("ui",arguments)},_Q:[]})}("apstag",window),apstag.init({pubID:"3226",adServer:"googletag",videoAdServer:"DFP",bidTimeout:800,gdpr:{cmpTimeout:700},deals:!0});var e=this.getDL(),t=document.createElement("script"),a=document.getElementsByTagName("script")[0];t.async=!0,t.src=e.src+e.path,a.parentNode.insertBefore(t,a);var r=document.createElement("link"),i=document.createElement("link");if(r.setAttribute("rel","dns-prefetch"),i.setAttribute("rel","preconnect"),r.src=e.src,i.src=e.src,a.parentNode.insertBefore(r,a),a.parentNode.insertBefore(i,a),null!=DTM.utils.getCookie("hem")&&"undefined"!=typeof apstag)if(void 0!==apstag.rpa)apstag.rpa({gdpr:{enabled:!0,consent:DTM.utils.getCookie("euconsent-v2")},hashedRecords:[{type:"email",record:DTM.utils.getCookie("hem")}],ttl:604800});else{setTimeout((function(){"undefined"!=typeof apstag&&void 0!==apstag.rpa&&apstag.rpa({gdpr:{enabled:!0,consent:DTM.utils.getCookie("euconsent-v2")},hashedRecords:[{type:"email",record:DTM.utils.getCookie("hem")}],ttl:604800})}),3e3)}}else void 0!==apstag.rpa&&null!=DTM.utils.getCookie("hem")&&apstag.rpa({gdpr:{enabled:!0,consent:DTM.utils.getCookie("euconsent-v2")},hashedRecords:[{type:"email",record:DTM.utils.getCookie("hem")}],ttl:604800})}catch(t){}this.trackedPV=!0,DTM.notify("PV tracked in tool <Amazon APS> (Data Layer)")}},target:{enabled:!0,dl:{},trackedPV:!1,getDL:function(){return this.dl},setDL:function(e){this.dl=e},init:function(){this.enabled=this.isEnabled(),this.enabled!=DTM.tools.DISABLED&&DTM.tools.list.push("target")},isEnabled:function(){return!0===DTM.config.atg_enabled?DTM.tools.ENABLED:DTM.tools.DISABLED},trackPV:function(){if(this.enabled!=DTM.tools.ENABLED||"undefined"==typeof adobe||void 0===adobe.target||"function"!=typeof adobe.target.getOffer||"function"!=typeof adobe.target.triggerView||"function"!=typeof adobe.target.trackEvent)return!1;adobe.target.trackEvent({mbox:"userTypeMBox",params:{userType:_satellite.getVar("user:type")}});var e={"epmas>suscripcion>confirmation":"orderConfirmPage","epmas>suscripcion>checkout":"orderCheckoutPage","epmas>suscripcion>payment":"orderPaymentPage"};if(e.hasOwnProperty(_satellite.getVar("subCategory2"))){var t={sku:_satellite.getVar("paywall:cartProduct"),transactionType:_satellite.getVar("paywall:transactionType")};"epmas>suscripcion>confirmation"==_satellite.getVar("subCategory2")&&(t.orderId=_satellite.getVar("paywall:transactionID")),adobe.target.trackEvent({mbox:e[_satellite.getVar("subCategory2")],params:t}),"epmas>suscripcion>confirmation"==_satellite.getVar("subCategory2")&&adobe.target.getOffer({mbox:"orderConfirm"+_satellite.getVar("paywall:cartProduct"),params:{sku:_satellite.getVar("paywall:cartProduct"),transactionType:_satellite.getVar("paywall:transactionType")},success:function(){},error:function(){}})}this.trackedPV=!0},trackEvent:function(e){if(this.enabled!=DTM.tools.ENABLED)return DTM.events.setEffect(e,"target",!1),!1;if(void 0===_satellite.getVar("event")[e])return DTM.notify("Target event past not valid <"+t+">","error"),!1;var t=_satellite.getVar("event")[e].eventInfo.eventName,a=_satellite.getVar("event")[e].attributes,r=!1;if(t==DTM.events.CHECKOUT){var i=a.hasOwnProperty("paywallTransactionType")&&"google"===a.paywallTransactionType?"orderCheckoutButtonSWG":"orderCheckoutButton";adobe.target.getOffer({mbox:i,params:{orderId:_satellite.getVar("paywall:transactionID"),"productPurchasedId ":_satellite.getVar("paywall:cartProduct")},success:function(){},error:function(){}}),r=!0}else if(t==DTM.events.BUTTONCLICK&&a.hasOwnProperty("buttonName")){var s={"epmas:checkout:pago":"orderCheckoutButton","epmas:checkout:chat:abrir:boton":"chatCheckoutButton","epmas:checkout:chat:abrir:icono":"chatCheckoutIcon","epmas:checkout:faq":"faqCheckoutButton","epmas:payment:pago":"orderPaymentButton","epmas:payment:chat:abrir:boton":"chatPaymentButton","epmas:payment:chat:abrir:icono":"chatPaymentIcon","epmas:payment:faq":"faqPaymentButton"};s.hasOwnProperty(a.buttonName)&&(adobe.target.getOffer({mbox:s[a.buttonName],params:{orderId:"","productPurchasedId ":_satellite.getVar("paywall:cartProduct")},success:function(){},error:function(){}}),r=!0)}else t==DTM.events.USERREGISTER&&(adobe.target.getOffer({mbox:"userRegisterOK",params:{originURL:a.hasOwnProperty("registerBackURL")?a.registerBackURL:location.href.replace(/[\?#].*?$/g,""),registerType:a.hasOwnProperty("registerType")?a.registerType:"not-set"},success:function(){},error:function(){}}),r=!0);return r&&DTM.notify("Event <"+t+"> tracked in tool <Target>"),DTM.events.setEffect(e,"target",r),r},trackAsyncPV:function(){this.enabled==DTM.tools.ENABLED&&"undefined"!=typeof adobe&&void 0!==adobe.target&&"function"==typeof adobe.target.triggerView&&adobe.target.triggerView(_satellite.getVar("pageName")),this.trackPV()}},wemass:{enabled:1,consents:-1,consentsID:968,trackedPV:!1,dl:{},init:function(){this.enabled=this.isEnabled()},getDL:function(){return this.dl},setDL:function(e){this.dl=e},lib:{init:function(){window.__wmass=window.__wmass||{},window.__wmass.bff=window.__wmass.bff||[],window.__wmass.getSegments=window.__wmass.getSegments||function(){try{pSegs=JSON.parse(window.localStorage._papns||"[]").slice(0,250).map(String)}catch(e){pSegs=[]}return{permutive:pSegs}};var e=document.createElement("script");e.src="https://service.wemass.com/dmp/30fcc5b151d263b41e36afc371fa61be.js",e.async=!0,document.body.appendChild(e)}},isEnabled:function(){this.canInitWemassByCountry()&&(window.didomiOnReady=window.didomiOnReady||[],window.didomiOnReady.push((function(){return-1!=Didomi.getUserStatus().vendors.consent.enabled.indexOf(968)?(DTM.tools.list.push("wemass"),DTM.tools.wemass.lib.init(),DTM.tools.wemass.trackedPV=DTM.tools.wemass.trackPV(),!0):-1==Didomi.getUserStatus().vendors.consent.disabled.indexOf(968)&&void Didomi.getObservableOnUserConsentStatusForVendor(this.consentID).subscribe((function(e){return void 0!==e&&(!0===e?(DTM.tools.list.push("wemass"),this.lib.init(),this.trackedPV=this.trackPV(),!0):!1!==e&&void 0)}))})))},canInitWemassByCountry:function(){var e="";DTM.utils.getCookie("arc-geo")?e=JSON.parse(DTM.utils.getCookie("arc-geo")).countrycode:DTM.utils.getCookie("pbsCountry")?e=DTM.utils.getCookie("pbsCountry"):DTM.utils.getCookie("eptz")?e=DTM.utils.getCookie("eptz"):"undefined"!=typeof PBS&&PBS.env.country&&(e=PBS.env.countryByTimeZone);return"ES"==e},getMeta:function(e){return"function"==typeof document.querySelectorAll&&document.querySelector('meta[name="'+e+'"]')&&document.querySelector('meta[name="'+e+'"]').content?document.querySelector('meta[name="'+e+'"]').content:""},trackPV:function(){if(this.enabled!=DTM.tools.ENABLED||!0===this.trackedPV)return!1;try{let e=[];digitalData.page.pageInfo.tags&&Array.isArray(digitalData.page.pageInfo.tags)&&digitalData.page.pageInfo.tags.forEach((t=>{t.name&&e.push(t.name)}));let t=[];return digitalData.page.pageInfo.author&&Array.isArray(digitalData.page.pageInfo.author)&&digitalData.page.pageInfo.author.forEach((e=>{e.name&&t.push(e.name)})),__wmass.bff.push((function(){"undefined"!=typeof digitalData&&(digitalData.user,1)&&void 0!==digitalData.user.profileID&&""!=digitalData.user.profileID&&__wmass.dmp.identify([{tag:"prisaProfile",id:digitalData.user.profileID}]),__wmass.dmp.addon("web",{page:{type:_satellite.getVar("pageType"),article:{topics:e,section:_satellite.getVar("primaryCategory"),subsection:_satellite.getVar("subCategory1"),description:DTM.tools.wemass.getMeta("description"),authors:t,id:digitalData.page.pageInfo.articleID},content:{categories:[_satellite.getVar("primaryCategory")]}}})})),DTM.notify("PV tracked in tool <wemass> (Data Layer)"),!0}catch(e){}this.trackedPV=!0,DTM.notify("PV tracked in tool <wemass> (Data Layer)")}},zeotap:{enabled:1,dl:{proId:"c54999bd-9dcc-4165-9bc7-565630567c7a",environment:"",filterId:"pruebaZeotap",consent:!0},consents:-1,consentsID:301,map:{consents:{}},lib:{init:function(){DTM.tools.zeotap.dl;!function(e,t){var a=t.createElement("script");a.type="text/javascript",a.crossorigin="anonymous",a.async=!0,a.src="https://content.zeotap.com/sdk/idp.min.js",a.onload=function(){},(t=t.getElementsByTagName("script")[0]).parentNode.insertBefore(a,t),function(e,t,a){for(var r=0;r<t.length;r++)!function(t){e[t]=function(){e[a].push([t].concat(Array.prototype.slice.call(arguments,0)))}}(t[r])}(t=e.zeotap||{_q:[],_qcmp:[]},["callMethod"],"_q"),e.zeotap=t,e.zeotap.callMethod("init",{partnerId:"c54999bd-9dcc-4165-9bc7-565630567c7a",useConsent:!0,checkForCMP:!1})}(window,document)}},trackedPV:!1,init:function(){window.didomiOnReady=window.didomiOnReady||[],window.didomiOnReady.push((function(){if(Didomi.getUserStatus().vendors.consent.enabled.indexOf(301)>-1){"fbia"==_satellite.getVar("platform")&&(window.ia_document={shareURL:_satellite.getVar("destinationURL"),referrer:_satellite.getVar("referringURL")});DTM.tools.zeotap.getDL();DTM.tools.zeotap.enabled=DTM.tools.zeotap.isEnabled();DTM.tools.zeotap.getDL();DTM.tools.zeotap.enabled!=DTM.tools.DISABLED&&(DTM.tools.list.push("zeotap"),window.didomiOnReady=window.didomiOnReady||[],window.didomiOnReady.push((function(){didomiState,didomiState.didomiVendorsConsentDenied,-1==didomiState.didomiVendorsConsentDenied.indexOf(":301,")&&(DTM.tools.zeotap.lib.init(),document.addEventListener("readystatechange",(()=>{"complete"==document.readyState?DTM.tools.zeotap.trackedPV=DTM.tools.zeotap.trackPV():window.addEventListener("DOMContentLoaded",(()=>{DTM.tools.zeotap.trackedPV=DTM.tools.zeotap.trackPV()}))})))}))),DTM.tools.zeotap.trackedPV=!0}window.didomiEventListeners=window.didomiEventListeners||[],window.didomiEventListeners.push({event:"consent.changed",listener:function(){if(Didomi.getUserStatus().vendors.consent.enabled.indexOf(301)>-1){"fbia"==_satellite.getVar("platform")&&(window.ia_document={shareURL:_satellite.getVar("destinationURL"),referrer:_satellite.getVar("referringURL")});DTM.tools.zeotap.getDL();DTM.tools.zeotap.enabled=DTM.tools.zeotap.isEnabled();DTM.tools.zeotap.getDL();DTM.tools.zeotap.enabled!=DTM.tools.DISABLED&&(DTM.tools.list.push("zeotap"),window.didomiOnReady=window.didomiOnReady||[],window.didomiOnReady.push((function(){didomiState,didomiState.didomiVendorsConsentDenied,-1==didomiState.didomiVendorsConsentDenied.indexOf(":301,")&&(DTM.tools.zeotap.lib.init(),document.addEventListener("readystatechange",(()=>{"complete"==document.readyState?DTM.tools.zeotap.trackedPV=DTM.tools.zeotap.trackPV():window.addEventListener("DOMContentLoaded",(()=>{DTM.tools.zeotap.trackedPV=DTM.tools.zeotap.trackPV()}))})))}))),DTM.tools.zeotap.trackedPV=!0}}})}))},getDL:function(){return this.dl},setDL:function(e){this.dl=e},isEnabled:function(){var e=DTM.utils.getQueryParam("zeotap_enabled"),t=void 0!==DTM.config.zeotap_enabled?DTM.config.zeotap_enabled:"1"==e||"0"!=e&&DTM.tools.allowAll;return!t||_satellite.getVar("platform")!=DTM.PLATFORM.AMP&&_satellite.getVar("platform")!=DTM.PLATFORM.FBIA&&_satellite.getVar("platform")!=DTM.PLATFORM.WIDGET||(t=!1),t=t?DTM.tools.ENABLED:DTM.tools.DISABLED,_satellite.getVar("platform")==DTM.PLATFORM.AMPPLAYER&&(t=DTM.tools.ONLYEVENTS),t},createMap:function(){this.map.consents[DTM.CONSENTS.WAITING]="",this.map.consents[DTM.CONSENTS.DEFAULT]="1",this.map.consents[DTM.CONSENTS.ACCEPT]="1",this.map.consents[DTM.CONSENTS.REJECT]="0"},trackPV:function(){if(this.enabled!=DTM.tools.ENABLED||!0===this.trackedPV)return!1;var e=this.getDL();void 0!==zeotap.setConsent&&(zeotap.setConsent(e.consent,7),zeotap.setUserIdentities({email:DTM.utils.getCookie("hem")},!0),DTM.notify("PV tracked in tool <zeotap> (Data Layer) consent: true")),this.trackedPV=!0}},critnam:{enabled:1,dl:{id:"PRRA_827_738_836",src:"prra.spxl.socy.es"},trackedPV:!1,init:function(){this.enabled=this.isEnabled();var e=this.enabled;window.didomiOnReady=window.didomiOnReady||[],window.didomiOnReady.push((function(){Didomi.getUserStatus().vendors.consent.enabled.indexOf(85)>-1&&e==DTM.tools.ENABLED&&_satellite.getVar("validPage")&&(!function(e,t,a,r){function i(a,r){var i;let s;i=function(){e.consenTag?e.consenTag.init({containerId:a,silentMode:!0},r||!1):console.warn("consenTag was not available")},(s=t.createElement("script")).src="https://consentag.eu/public/3.1.1/consenTag.js",s.async=!0,s.onload=i,t.head.appendChild(s)}r=r||2,!0?e.__tcfapi("ping",r,(function(t){t.cmpLoaded&&(t.gdprApplies?e.__tcfapi("addEventListener",r,(function(e,t){t&&("useractioncomplete"===e.eventStatus||"tcloaded"===e.eventStatus)&&e.tcString&&i(a,e.tcString)})):i(a,!0))})):i(a,!0)}(window,document,"79722161",2),DTM.tools.list.push("critnam")),window.didomiEventListeners=window.didomiEventListeners||[],window.didomiEventListeners.push({event:"consent.changed",listener:function(){Didomi.getUserStatus().vendors.consent.enabled.indexOf(85)>-1&&e==DTM.tools.ENABLED&&_satellite.getVar("validPage")&&(!function(e,t,a,r){function i(a,r){var i;let s;i=function(){e.consenTag?e.consenTag.init({containerId:a,silentMode:!0},r||!1):console.warn("consenTag was not available")},(s=t.createElement("script")).src="https://consentag.eu/public/3.1.1/consenTag.js",s.async=!0,s.onload=i,t.head.appendChild(s)}r=r||2,!0?e.__tcfapi("ping",r,(function(t){t.cmpLoaded&&(t.gdprApplies?e.__tcfapi("addEventListener",r,(function(e,t){t&&("useractioncomplete"===e.eventStatus||"tcloaded"===e.eventStatus)&&e.tcString&&i(a,e.tcString)})):i(a,!0))})):i(a,!0)}(window,document,"79722161",2),DTM.tools.list.push("critnam"))}})}))},isEnabled:function(){let e=void 0!==DTM.config.critnam_enabled?DTM.config.critnam_enabled:DTM.tools.allowAll;return!e||_satellite.getVar("platform")!=DTM.PLATFORM.AMP&&_satellite.getVar("platform")!=DTM.PLATFORM.FBIA&&_satellite.getVar("platform")!=DTM.PLATFORM.WIDGET||(e=!1),e=e?DTM.tools.ENABLED:DTM.tools.DISABLED,e},trackPV:function(){return this.enabled==DTM.tools.ENABLED&&!0!==this.trackedPV&&(this.trackedPV=!0,DTM.notify("PV tracked in tool <critnam> (Data Layer)"),!0)}},nicequest:{enabled:1,dl:{},trackedPV:!1,consents:-1,consentsID:1296,init:function(){this.enabled=this.isEnabled(),this.enabled!=DTM.tools.DISABLED&&DTM.tools.list.push("nicequest"),this.consents=DTM.CONSENTS.DEFAULT,this.setDL({src:{domain:"https://mpc.nicequest.com",end_point:"/mpc/ConsumerServlet"},parameters:{p:"FLUZES_261164",s:"PRISA",gdpr:"{GDPR}",gdpr_consent:"{GDPR_CONSENT_1296}"}})},getDL:function(){return this.dl},setDL:function(e){this.dl=e},isEnabled:function(){return window.location.href.indexOf("clima-y-medio-ambiente")>-1||"https://elpais.com/"==window.location.href},trackPV:function(){if(this.enabled!=DTM.tools.ENABLED||this.consents!==DTM.CONSENTS.ACCEPT)return!1;var e=this.getDL();DTM.utils.sendBeacon(e.src.domain+e.src.end_point,e.parameters,!1,!1,!0),this.trackedPV=!0},trackAsyncPV:function(){this.trackPV()}}},trackGDPRPV:function(e,t){var a=DTM.tools[e].consentsID;"undefined"!=typeof Didomi&&"function"==typeof Didomi.getObservableOnUserConsentStatusForVendor?Didomi.getObservableOnUserConsentStatusForVendor(a).subscribe((function(a){DTM.tools[e].consents=void 0===a?DTM.CONSENTS.WAITING:!0===a?DTM.CONSENTS.ACCEPT:DTM.CONSENTS.REJECT,!1!==DTM.tools[e].trackPV()&&DTM.notify("PV tracked in tool <"+e+"> ("+t+")")})):void 0!==window.gdprAppliesGlobally?function(e){window.didomiOnReady=window.didomiOnReady||[],window.didomiOnReady.push((function(){Didomi.getObservableOnUserConsentStatusForVendor(a).subscribe((function(t){DTM.tools[e].consents=void 0===t?DTM.CONSENTS.WAITING:!0===t?DTM.CONSENTS.ACCEPT:DTM.CONSENTS.REJECT,DTM.tools[e].trackPV()}))}))}(e):(DTM.tools[e].consents=DTM.CONSENTS.DEFAULT,DTM.tools[e].trackPV())},trackPV:function(){if(DTM.tools.initialized)for(var e in this.tools.list){var t=this.tools.list[e];if(this.tools.hasOwnProperty(t)&&"function"==typeof this.tools[t].trackPV)if(void 0!==this.tools[t].consentsID&&void 0!==window.gdprAppliesGlobally)DTM.trackGDPRPV(t,"data layer + consents");else!1!==DTM.tools[t].trackPV()&&DTM.notify("PV tracked in tool <"+t+"> (data layer)")}else this.notify("Uninitialized tools")},trackAsyncPV:function(){var e=_satellite.getVar("pageName");if(DTM.dateInit=new Date,DTM.internalTest="",DTM.dataLayer.asyncPV=!0,DTM.dataLayer.init(),e==_satellite.getVar("pageName")&&"epmas"==_satellite.getVar("primaryCategory"))return DTM.notify("Async PV duplicate (not tracked)","warn"),!1;for(var t in this.tools.list){var a=this.tools.list[t];if(this.tools.hasOwnProperty(a)&&void 0!==this.tools[a].trackAsyncPV)!1!==this.tools[a].trackAsyncPV()&&DTM.notify("Async PV tracked in tool <"+a+"> (async)")}},trackEvent:function(e,t){if(this.notify("DTM.trackEvent fired <"+e+">",!0),"string"==typeof e&&(void 0===t||"object"==typeof t))if(this.tools.initialized)if(this.events.validEvent(e))if(("videoPaused"==e||"audioPaused"==e)&&t.hasOwnProperty("currentTime")&&t.hasOwnProperty("mediaDuration")&&parseInt(t.currentTime)>0&&parseInt(t.mediaDuration)-parseInt(t.currentTime)<2)DTM.notify("Event not valid <"+e+">");else if((t=this.utils.formatData(t)).hasOwnProperty("validEvent")||e!=DTM.events.USERLOGIN&&e!=DTM.events.USERREGISTER){var a=window.digitalData.event.length;for(var r in window.digitalData.event.push({eventInfo:{eventName:e,eventAction:e,timeStamp:new Date,effect:[]},category:{primaryCategory:_satellite.getVar("primaryCategory"),subCategory1:_satellite.getVar("subCategory1"),pageType:_satellite.getVar("pageType")},attributes:t}),DTM.tools.list){var i=DTM.tools.list[r];"object"==typeof DTM.tools[i]&&"function"==typeof DTM.tools[i].trackEvent&&DTM.tools[i].trackEvent(a)}}else DTM.notify("Event from page not valid <"+e+">","error");else DTM.notify("Event not valid <"+e+">","error");else 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i=t.destinations,n="",d=[],o=0;o<i.length;o++)for(var l in i[o])if("marfeel"==i[o].alias){n=i[o].segments;for(var r=0;r<n.length;r++)d.push(n[r].id);break}window.marfeel=window.marfeel||{cmd:[]},0==d.length?window.marfeel.cmd.push(["compass",function(e){e.clearUserSegments()}]):window.marfeel.cmd.push(["compass",function(e){e.setUserSegments(d)}]);var m={};i=t.destinations;if(""!=s||""!=a)for(""!=s&&(m[s]={}),m[a]={},o=0;o<i.length;o++)if(""!=s&&"arcid"==i[o].alias.split("|")[1])for(m[s][i[o].alias]=[],r=0;r<i[o].segments.length;r++){var p='{"id":"'+i[o].segments[r].id+'"}';m[s][i[o].alias].push(JSON.parse(p))}else for(m[a][i[o].alias]=[],r=0;r<i[o].segments.length;r++){p='{"id":"'+i[o].segments[r].id+'"}';m[a][i[o].alias].push(JSON.parse(p))}else for(m[ecid]={},o=0;o<i.length;o++)for(m[ecid][i[o].alias]=[],r=0;r<i[o].segments.length;r++){p='{"id":"'+i[o].segments[r].id+'"}';m[ecid][i[o].alias].push(JSON.parse(p))}m.lastUpdated=Date.now();let c=new 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Author response:
The following is the authors’ response to the original reviews.
Public Reviews:
Reviewer #1 (Public Review):
The manuscript by Li et al. investigates the metabolism-independent role of nuclear IDH1 in chromatin state reprogramming during erythropoiesis. The authors describe accumulation and redistribution of histone H3K79me3, and downregulation of SIRT1, as a cause for dyserythropoiesis observed due to IDH1 deficiency. The authors studied the consequences of IDH1 knockdown, and targeted knockout of nuclear IDH1, in normal human erythroid cells derived from hematopoietic stem and progenitor cells and HUDEP2 cells respectively. They further correlate some of the observations such as nuclear localization of IDH1 and aberrant localization of histone modifications in MDS and AML patient samples harboring IDH1 mutations. These observations are intriguing from a mechanistic perspective and they hold therapeutic significance, however there are major concerns that make the inferences presented in the manuscript less convincing.
(1) The authors show the presence of nuclear IDH1 both by cell fractionation and IF, and employ an efficient strategy to knock out nuclear IDH1 (knockout IDH1/ Sg-IDH1 and rescue with the NES tagged IDH1/ Sg-NES-IDH1 that does not enter the nucleus) in HUDEP2 cells. However, some important controls are missing.
A) In Figure 3C, for IDH1 staining, Sg-IDH1 knockout control is missing.
Thanks for the reviewer’s suggestion. We have complemented the staining of Sg-IDH1 knockout cells, and made corresponding revision in Figure 3C in the revised manuscript.
B) Wild-type IDH1 rescue control (ie., IDH1 without NES tag) is missing to gauge the maximum rescue that is possible with this system.
Thanks for the reviewer’s suggestion. We have overexpressed wild-type IDH1 in the IDH1-deficient HUDEP2 cell line and detected the phenotype. The results are presented in Supplementary Figure 9 in the revised manuscript. As shown in Supplementary Figure 9A, IDH1 deficiency resulted in reduced cell number in HUDEP2 cells, a phenotype that was rescued by overexpression of wild-type IDH1 but not by NES-IDH1. Given IDH1's well-established role in redox homeostasis through catalyzing isocitrate to α-KG conversion, we hypothesized that both wild-type IDH1 and NES-IDH1 overexpression would significantly restore α-KG levels compared to the IDH1-deficient group. Supplementary Figure 9B demonstrates that IDH1 depletion resulted in a dramatic decrease in α-KG levels, whereas overexpression of either wild-type IDH1 or NES-IDH1 almost completely restored α-KG levels, as anticipated. These results suggest that wild-type IDH1 overexpression can restore metabolic regulatory functions as effectively as NES-IDH1 overexpression. To investigate whether apoptosis contributes to the impaired cell expansion caused by IDH1 deficiency, we performed Annexin V/PI staining to quantify apoptotic cells. As shown in Supplementary Figure 9C and D, flow cytometry analysis revealed no significant changes in apoptosis rates following either IDH1 depletion or ectopic expression of wild-type IDH1 or NES-IDH1 in IDH1 deficient HUDEP2 cells.
Flow cytometric analysis demonstrated that IDH1 deficiency triggered S-phase accumulation at day 8, indicative of cell cycle arrest. Whereas ectopic expression of wild-type IDH1 significantly rescued this cell cycle defect, overexpression of NES-IDH1 failed to ameliorate the S-phase accumulation phenotype induced by IDH1 depletion, as presented in Supplementary Figure 9E and F. Although NES-IDH1 overexpression rescued metabolic regulatory function defect, it failed to alleviate the cell cycle arrest induced by IDH1 deficiency. In contrast, wild-type IDH1 overexpression fully restored normal cell cycle progression. This functional dichotomy demonstrates that nuclear-localized IDH1 executes critical roles distinct from its cytoplasmic counterpart, and overexpression of wild-type IDH1 could efficient restore the functional impairment induced by depletion of nuclear localized IDH1.
(2) Considering the nuclear knockout of IDH1 (Sg-NES-IDH1 referenced in the previous point) is a key experimental system that the authors have employed to delineate non-metabolic functions of IDH1 in human erythropoiesis, some critical experiments are lacking to make convincing inferences.
A) The authors rely on IF to show the nuclear deletion of Sg-NES-IDH1 HUDEP2 cells. As mentioned earlier since a knockout control is missing in IF experiments, a cellular fractionation experiment (similar to what is shown in Figure 2F) is required to convincingly show the nuclear deletion in these cells.
We sincerely thank the reviewer for raising this critical point. As suggested, we have performed additional IF experiments and cellular fractionation experiments to comprehensively address the subcellular localization of IDH1.
The results of IF staining were shown in Figure 3C of the revised manuscript. In Control HUDEP2 cells, endogenous IDH1 was detected in both the cytoplasm and nucleus. This dual localization may reflect its dynamic roles in cytoplasmic metabolic processes and potential nuclear functions under specific conditions. In Sg-IDH1 cells (IDH1 knockout), IDH1 signal was undetectable, confirming efficient depletion of the protein. In Sg-NES-IDH1 cells (overexpressing NES-IDH1 in IDH1 deficient cells), IDH1 predominantly accumulated in the cytoplasm, consistent with the disruption of its nuclear export signal. The dual localization of IDH1 that was determined by IF staining experiment were then further confirmed by cellular fractionation assays, as shown in Figure 3D.
B) Since the authors attribute nuclear localization to a lack of metabolic/enzymatic functions, it is important to show the status of ROS and alpha-KG in the Sg-NES-IDH1 in comparison to control, wild type rescue, and knockout HUDEP2 cells. The authors observe an increase of ROS and a decrease of alpha-KG upon IDH1 knockdown. If nuclear IDH1 is not involved in metabolic functions, is there only a minimal or no impact of the nuclear knockout of IDH1 on ROS and alpha-KG, in comparison to complete knockout? These studies are lacking.
We appreciate the insightful suggestions of the reviewers and agree that the detection of ROS and alpha-KG is useful for the demonstration of the non-canonical function of IDH1. We examined alpha-KG concentrations in control, IDH1 knockout and nuclear IDH1 knockout HUDEP2 cell lines. The results showed a significant decrease in alpha-KG content after complete knockout of IDH1, whereas there was no significant change in nuclear knockout IDH1 (Supplementary Figure 9B). As to the detection of ROS level, the commercial ROS assay kits that we can get are detected using PE (Excitation: 565nm; Emission: 575nm) and FITC (Excitation: 488nm; Emission: 518nm) channels in flow cytometry. We constructed HUDEP2 cell lines of Sg-IDH1 and Sg-NES-IDH1 to express green fluorescent protein (Excitation: 488nm; Emission: 507nm) and Kusabira Orange fluorescent protein (Excitation: 500nm; Emission: 561nm) by themselves. Unfortunately, due to the spectral overlap of the fluorescence channels, we were unable to detect the changes in ROS levels in these HUDEP2 cell lines using the available commercial kit.
(3) The authors report abnormal nuclear phenotype in IDH1 deficient erythroid cells. It is not clear what parameters are used here to define and quantify abnormal nuclei. Based on the cytospins (eg., Figure 1A, 3D) many multinucleated cells are seen in both shIDH1 and Sg-NES-IDH1 erythroid cells, compared to control cells. Importantly, this phenotype and enucleation defects are not rescued by the administration of alpha-KG (Figures 1E, F). The authors study these nuclei with electron microscopy and report increased euchromatin in Figure 4B. However, there is no discussion or quantification of polyploidy/multinucleation in the IDH1 deficient cells, despite their increased presence in the cytospins.
A) PI staining followed by cell cycle FACS will be helpful in gauging the extent of polyploidy in IDH1 deficient cells and could add to the discussions of the defects related to abnormal nuclei.
We appreciate the reviewer’s insightful suggestion. Since PI dye is detected using the PE channel (Excitation: 565nm; Emission: 575nm) of the flow cytometer and the HUDEP2 cell line expresses Kusabira orange fluorescent protein (Excitation: 500nm; Emission: 561nm), we were unable to use PI staining to detect the cell cycle. Edu staining is another commonly used method to determine cell cycle progression, and we performed Edu staining followed by flow cytometry analysis on Control, Sg-IDH1 and Sg-NES-IDH1 HUDEP2 cells, respectively. The results showed that complete knockdown of IDH1 resulted in S-phase block and increased polyploidy in HUDEP2 cells on day 8 of erythroid differentiation, and overexpression of IDH1-NES did not reverse this phenotype (Supplemental Figure 9E-F). Moreover, we have added a discussion of abnormal nuclei being associated with impaired erythropoiesis.
B) For electron microscopy quantification in Figures 4B and C, how the quantification was done and the labelling of the y-axis (% of euchromatin and heterochromatin) in Figure 4 C is not clear and is confusingly presented. The details on how the quantification was done and a clear label (y-axis in Figure 4C) for the quantification are needed.
Thanks for the reviewer's suggestion. In this study, we calculated the area of nuclear, heterochromatin and euchromatin by using Image J software. We addressed the quantification strategy in the section of Supplementary methods of the revised Supplementary file. In addition, the y-axis label in Figure 4C was changed to “the area percentage of euchromatin and heterochromatin’’.
C) As mentioned earlier, what parameters were used to define and quantify abnormal nuclei (e.g. Figure 1A) needs to be discussed clearly. The red arrows in Figure 1A all point to bi/multinucleated cells. If this is the case, this needs to be made clear.
We thank the reviewer for their suggestion. In our present study, nuclear malformations were defined as cells exhibiting binucleation or multinucleation based on cytospin analysis. A minimum of 300 cells per group were evaluated, and the proportion of aberrant nuclei was calculated as (number of abnormal cells / total counted cells) × 100%.
(4) The authors mention that their previous study (reference #22) showed that ROS scavengers did not rescue dyseythropoiesis in shIDH1 cells. However, in this referenced study they did report that vitamin C, a ROS scavenger, partially rescued enucleation in IDH1 deficient cells and completely suppressed abnormal nuclei in both control and IDH1 deficient cells, in addition to restoring redox homeostasis by scavenging reactive oxygen species in shIDH1 erythroid cells. In the current study, the authors used ROS scavengers GSH and NAC in shIDH1 erythroid cells and showed that they do not rescue abnormal nuclei phenotype and enucleation defects. The differences between the results in their previous study with vitamin C vs GSH and NAC in the context of IDH1 deficiency need to be discussed.
We appreciate the reviewer’s insightful observation. The apparent discrepancy between the effects of vitamin C (VC) in our previous study and glutathione (GSH)/N-acetylcysteine (NAC) in the current work can be attributed to divergent molecular mechanisms beyond ROS scavenging. A growing body of evidence has identified vitamin C as a multifunctional regulator. In addition to acting as an antioxidant maintaining redox homeostasis, VC also acts as a critical epigenetic modulator. VC have been identified as a cofactor for α-ketoglutarate (α-KG)-dependent dioxygenases, including TET2, which catalyzes 5-methylcytosine (5mC) oxidation to 5-hydroxymethylcytosine (5hmC) [1,2]. Structural studies confirm its direct interaction with TET2’s catalytic domain to enhance enzymatic activity in vitro [3]. The biological significance of the epigenetic modulation induced by vitamin C is illustrated by its ability to improve the generation of induced pluripotent stem cells and to induce a blastocyst-like state in mouse embryonic stem cells by promoting demethylation of H3K9 and 5mC, respectively [4,5]. In contrast, GSH and NAC are canonical ROS scavengers lacking intrinsic epigenetic-modifying activity. While they effectively neutralize oxidative stress (as validated by reduced ROS levels in our current data, Supplemental Figure 7), their inability to rescue nuclear abnormalities or enucleation defects in IDH1 deficient cells suggests that IDH1 deficiency-driven dyserythropoiesis is not solely ROS-dependent.
References:
(1) Blaschke K, Ebata KT, Karimi MM, Zepeda-Martínez JA, Goyal P, et al. Vitamin C induces Tet-dependent DNA demethylation and a blastocyst-like state in ES cells. Nature. 20138;500(7461): 222-226.
(2) Minor EA, Court BL, Young JI, Wang G. Ascorbate induces ten-eleven translocation (Tet) methylcytosine dioxygenase-mediated generation of 5-hydroxymethylcytosine. J Biol Chem. 2013;288(19): 13669-13674.
(3) Yin R, Mao S, Zhao B, Chong Z, Yang Y, et al. Ascorbic acid enhances Tet-mediated 5-methylcytosine oxidation and promotes DNA demethylation in mammals. J Am Chem Soc. 2013;135(28):10396-10403.
(4) Esteban MA, Wang T, Qin B, Yang J, Qin D, et al. Vitamin C enhances the generation of mouse and human induced pluripotent stem cells. Cell Stem Cell. 2010;6(1):71-79.
(5) Chung T, Brena RM, Kolle G, Grimmond SM, Berman BP, et al. Vitamin C promotes widespread yet specific DNA demethylation of the epigenome in human embryonic stem cells. Stem Cells. 2010;28(10):1848-1855.
(5) The authors describe an increase in euchromatin as the consequential abnormal nuclei phenotype in shIDH1 erythroid cells. However, in their RNA-seq, they observe an almost equal number of genes that are up and down-regulated in shIDH1 cells compared to control cells. If possible, an RNA-Seq in nuclear knockout Sg-NES-IDH1 erythroid cells in comparison with knockout and wild-type cells will be helpful to tease out whether a specific absence of IDH1 in the nucleus (ie., lack of metabolic functions of IDH) impacts gene expression differently.
Thanks for the reviewer's suggestion. ATAC-seq showed an increase in chromatin accessibility after IDH1 deletion, but the number of up-regulated genes was slightly larger than that of down-regulated genes, which may be caused by the metabolic changes affected by IDH1 deletion. In order to explore the effect of chromatin accessibility changes on gene expression after IDH1 deletion, we analyzed the changes in differential gene expression at the differential ATAC peak region (as shown in Author response image 1), and the results showed that the gene expression at the ATAC peak region with increased chromatin accessibility was significantly up-regulated. This may explain the regulation of chromatin accessibility on gene expression.
Author response image 1.
Box plots of gene expression differences of differential ATAC peaks located in promoter for the signal increasing and decreasing groups.
(6) In Figure 8, the authors show data related to SIRT1's role in mediating non-metabolic, chromatin-associated functions of IDH1.
A) The authors show that SIRT1 inhibition leads to a rescue of enucleation and abnormal nuclei. However, whether this rescues the progression through the late stages of terminal differentiation and the euchromatin/heterochromatin ratio is not clear.
Thanks for the reviewer's suggestion. As shown in Supplementary Figure 14 and 15 in the revised Supplementary Data, our data showed that both the treatment of SRT1720 on normal erythroid cells and treatment of IDH1-deficient erythroid cells with SIRT1 inhibitor both have no effect on the terminal differentiation.
(7) In Figure 4 and Supplemental Figure 8, the authors show the accumulation and altered cellular localization of H3K79me3, H3K9me3, and H3K27me2, and the lack of accumulation of other three histone modifications they tested (H3K4me3, H3K35me4, and H3K36me2) in shIDH1 cells. They also show the accumulation and altered localization of the specific histone marks in Sg-NES-IDH1 HUDEP2 cells.
A) To aid better comparison of these histone modifications, it will be helpful to show the cell fractionation data of the three histone modifications that did not accumulate (H3K4me3, H3K35me4, and H3K36me2), similar to what was shown in Figure 4E for H3K79me3, H3K9me3, and H3K27me2).
We appreciate the reviewer’s insightful suggestion. We collected erythroblasts on day 15 of differentiation from cord blood-derived CD34<sup>+</sup> hematopoietic stem cells to erythroid lineage and performed ChIP assay. As shown in Author response image 2, the results showed that the concentration of bound DNA of H3K9me3, H3K27me2 and H3K79me3 was too low to meet the sequencing quality requirement, which was consistent with that of WB. In addition, we tried to perform ChIP-seq for H3K79me3, and the results showed that there was no marked peak signal.
Author response image 2.
ChIP-seq analysis show that there was no marked peak signal of H3K79me3 on D15. (A) Quality control of ChIP assay for H3K9me3, H3K27me2, and H3K79me3. (B) Representative peaks chart image showed normalized ChIP signal of H3K79me3 at gene body regions. (C) Heatmaps displayed normalized ChIP signal of H3K79me3 at gene body regions. The window represents ±1.5 kb regions from the gene body. TES, transcriptional end site; TSS, transcriptional start site.
C) Among the three histone marks that are dysregulated in IDH1 deficient cells (H3K79me3, H3K9me3, and H3K27me2), the authors show via ChIP-seq (Fig5) that H3K79me3 is the critical factor. However, the ChIP-seq data shown here lacks many details and this makes it hard to interpret the data. For example, in Figure 5A, they do not mention which samples the data shown correspond to (are these differential peaks in shIDH1 compared to shLuc cells?). There is also no mention of how many replicates were used for the ChIP seq studies.
We thank the reviewer for pointing this out. We apologize for not clearly describing the ChIP-seq data for H3K9me3, H3K27me2 and H3K79me3 and we have revised them in the corresponding paragraphs. Since H3 proteins gradually translocate from the nucleus to the cytoplasm starting at day 11 (late Baso-E/Ploy-E) of erythroid lineage differentiation, we performed ChIP-seq for H3K9me3, H3K27me2 and H3K79me3 only for the shIDH1 group, and set up three independent biological replicates for each of them.
Reviewer #2 (Public Review):
Li and colleagues investigate the enzymatic activity-independent function of IDH1 in regulating erythropoiesis. This manuscript reveals that IDH1 deficiency in the nucleus leads to the redistribution of histone marks (especially H3K79me3) and chromatin state reprogramming. Their findings suggest a non-typical localization and function of the metabolic enzyme, providing new insights for further studies into the non-metabolic roles of metabolic enzymes. However, there are still some issues that need addressing:
(1) Could the authors show the RNA and protein expression levels (without fractionation) of IDH1 on different days throughout the human CD34+ erythroid differentiation?
We sincerely appreciate the reviewer’s constructive feedback. To address this point, we have now systematically quantified IDH1 expression dynamics across erythropoiesis stages using qRT-PCR and Western blot analyses. As quantified in Supplementary fige 1, IDH1 expression exhibited a progressive upregulation during early erythropoiesis and subsequently stabilized throughout terminal differentiation.
(2) Even though the human CD34+ erythroid differentiation protocol was published and cited in the manuscript, it would be helpful to specify which erythroid stages correspond to cells on days 7, 9, 11, 13, and 15.
We sincerely thank the reviewer for raising this important methodological consideration. Our research group has previously established a robust platform for staged human erythropoiesis characterization using cord blood-derived CD34<sup>+</sup> hematopoietic stem cells (HSCs) [6-9]. This standardized protocol enables high-purity isolation and functional analysis of erythroblasts at defined differentiation stages.
Thanks for the reviewer’s suggestion. Our previous work (Jingping Hu et.al, Blood 2013. Xu Han et.al, Blood 2017.Yaomei Wang et.al, Blood 2021.) have isolation and functional characterization of human erythroblasts at distinct stages by using Cord blood. These works illustrated that using cord blood-derived hematopoietic stem cells and purification each stage of human erythrocytes can facilitate a comprehensive cellular and molecular characterization.
Following isolation from cord blood, CD34<sup>+</sup> cells were cultured in a serum-free medium and induced to undergo erythroid differentiation using our standardized protocol. The process of erythropoiesis was comprised of 2 phases. During the early phase (day 0 to day 6), hematopoietic stem progenitor cells expanded and differentiated into erythroid progenitors, including BFU-E and CFU-E cells.
During terminal erythroid maturation (day 7 to day 15), CFU-E cells progressively transitioned through defined erythroblast stages, as validated by daily cytospin morphology and expression of band 3/α4 integrin. The stage-specific composition was quantitatively characterized as follows:
Author response table 1.
The composition of erythroblast during terminal stage erythropoiesis.
This differentiation progression from proerythroblasts (Pro-E) through basophilic (Baso-E), polychromatic (Poly-E), to orthochromatic erythroblasts (Ortho-E) recapitulates physiological human erythropoiesis, confirming the validity of our differentiation system for mechanistic studies.
Reference:
(6) Li J, Hale J, Bhagia P, Xue F, Chen L, et al. Isolation and transcriptome analyses of human erythroid progenitors: BFU-E and CFU-E. Blood. 2014;124(24):3636-3645.
(7) Hu J, Liu J, Xue F, Halverson G, Reid M, et al. Isolation and functional characterization of human erythroblasts at distinct stages: implications for understanding of normal and disordered erythropoiesis in vivo. Blood. 2013;121(16):3246-3253.
(8) Wang Y, Li W, Schulz VP, Zhao H, Qu X, et al. Impairment of human terminal erythroid differentiation by histone deacetylase 5 deficiency. Blood. 2021;138(17):1615-1627.
(9) Li M, Liu D, Xue F, Zhang H, Yang Q, et al. Stage-specific dual function: EZH2 regulates human erythropoiesis by eliciting histone and non-histone methylation. Haematologica. 2023;108(9):2487-2502.
(3) It is important to mention on which day the lentiviral knockdown of IDH1 was performed. Will the phenotype differ if the knockdown is performed in early vs. late erythropoiesis? In Figures 1C and 1D, on which day do the authors begin the knockdown of IDH1 and administer NAC and GSH treatments?
We sincerely appreciate the reviewer’s inquiry regarding the experimental timeline. The day of getting CD34<sup>+</sup> cells was recorded as day 0. Lentivirus of IDH1-shRNA and Luciferase -shRNA was transduced in human CD34<sup>+</sup> at day 2. Puromycin selection was initiated 24h post-transduction to eliminate non-transduced cells. IDH1-KD cells were then selected for 3 days. The knock down deficiency of IDH1 was determined on day 7. NAC or GSH was added to culture medium and replenished every 2 days.
(4) While the cell phenotype of IDH1 deficiency is quite dramatic, yielding cells with larger nuclei and multi-nuclei, the authors only attribute this phenotype to defects in chromatin condensation. Is it possible that IDH1-knockdown cells also exhibit primary defects in mitosis/cytokinesis (not just secondary to the nuclear condensation defect)?), given the function of H3K79Me in cell cycle regulation?
We appreciate the reviewer’s insightful suggestion. We performed Edu based cell cycle analysis on Control, Sg-IDH1 and Sg-NES-IDH1 HUDEP2 cells, respectively. The results showed that IDH1 deficiency resulted in S-phase block and increased polyploidy in HUDEP2 cells on day 8 of erythroid differentiation. NES-IDH1 overexpression failed to rescue these defects, indicating nuclear IDH1 depletion as the primary driving factor (Figure 3E,F). Recent studies have established a clear link between cell cycle arrest and nuclear malformation. Chromosome mis-segregation, nuclear lamina disruption, mechanical stress on the nuclear envelope, and nucleolar dysfunction all contribute to nuclear abnormalities that trigger cell cycle checkpoints [10,11]. Based on all these findings, it reasonable for us to speculate that the cell cycle defect in IDH1 deficient cells might caused by the nuclear malfunction.
Reference:
(10) Hong T, Hogger AC, Wang D, Pan Q, Gansel J, et al. Cell Death Discov. CDK4/6 inhibition initiates cell cycle arrest by nuclear translocation of RB and induces a multistep molecular response. 2024;10(1):453.
(11) Hervé S, Scelfo A, Marchisio GB, Grison M, Vaidžiulytė K, et al. Chromosome mis-segregation triggers cell cycle arrest through a mechanosensitive nuclear envelope checkpoint. Nat Cell Biol. 2025;27(1):73-86.
(5) Why are there two bands of Histone H3 in Figure 4A?
We sincerely appreciate the reviewer's insightful observation regarding the dual bands of Histone H3 in our original Figure 4A. Upon rigorous investigation, we identified that the observed doublet pattern likely originated from the inter-batch variability of the original commercial antibody. To conclusively resolve this technical artifact, we have procured a new lot of Histone H3 antibody and repeated the western blot experimental under optimized conditions, and the results demonstrates a single band of H3.
(6) Displaying a heatmap and profile plots in Figure 5A between control and IDH1-deficient cells will help illustrate changes in H3K79me3 density in the nucleus after IDH1 knockdown.
Thank you for your suggestion. As presented in Author response image 2, we performed ChIP assays on erythroblasts collected at day 15. However, the concentration of H3K79me3-bound DNA was insufficient to meet the quality threshold required for reliable sequencing. Consequently, we are unable to generate the requested heatmap and profile plots due to limitations in data integrity from this experimental condition.
Reviewer #3 (Public Review):
Li, Zhang, Wu, and colleagues describe a new role for nuclear IDH1 in erythroid differentiation independent from its enzymatic function. IDH1 depletion results in a terminal erythroid differentiation defect with polychromatic and orthochromatic erythroblasts showing abnormal nuclei, nuclear condensation defects, and an increased proportion of euchromatin, as well as enucleation defects. Using ChIP-seq for the histone modifications H3K79me3, H3K27me2, and H3K9me3, as well as ATAC-seq and RNA-seq in primary CD34-derived erythroblasts, the authors elucidate SIRT1 as a key dysregulated gene that is upregulated upon IDH1 knockdown. They furthermore show that chemical inhibition of SIRT1 partially rescues the abnormal nuclear morphology and enucleation defect during IDH1-deficient erythroid differentiation. The phenotype of delayed erythroid maturation and enucleation upon IDH1 shRNA-mediated knockdown was described in the group's previous co-authored study (PMID: 33535038). The authors' new hypothesis of an enzyme- and metabolism-independent role of IDH1 in this process is currently not supported by conclusive experimental evidence as discussed in more detail further below. On the other hand, while the dependency of IDH1 mutant cells on NAD+, as well as cell survival benefit upon SIRT1 inhibition, has already been shown (see, e.g, PMID: 26678339, PMID: 32710757), previous studies focused on cancer cell lines and did not look at a developmental differentiation process, which makes this study interesting.
(1) The central hypothesis that IDH1 has a role independent of its enzymatic function is interesting but not supported by the experiments. One of the author's supporting arguments for their claim is that alpha-ketoglutarate (aKG) does not rescue the IDH1 phenotype of reduced enucleation. However, in the group's previous co-authored study (PMID: 33535038), they show that when IDH1 is knocked down, the addition of aKG even exacerbates the reduced enucleation phenotype, which could indicate that aKG catalysis by cytoplasmic IDH1 enzyme is important during terminal erythroid differentiation. A definitive experiment to test the requirement of IDH1's enzymatic function in erythropoiesis would be to knock down/out IDH1 and re-express an IDH1 catalytic site mutant. The authors perform an interesting genetic manipulation in HUDEP-2 cells to address a nucleus-specific role of IDH1 through CRISPR/Cas-mediated IDH1 knockout followed by overexpression of an IDH1 construct containing a nuclear export signal. However, this system is only used to show nuclear abnormalities and (not quantified) accumulation of H3K79me3 upon nuclear exclusion of IDH1. Otherwise, a global IDH1 shRNA knockdown approach is employed, which will affect both forms of IDH1, cytoplasmic and nuclear. In this system and even the NES-IDH1 system, an enzymatic role of IDH1 cannot be excluded because (1) shRNA selection takes several days, prohibiting the assessment of direct effects of IDH1 loss of function (only a degron approach could address this if IDH1's half-life is short), and (2) metabolic activity of this part of the TCA cycle in the nucleus has recently been demonstrated (PMID: 36044572), and thus even a nuclear role of IDH1 could be linked to its enzymatic function, which makes it a challenging task to separate two functions if they exist.
We appreciate the reviewer’s emphasis on rigorously distinguishing between enzymatic and enzymatic independent roles of IDH1. In our revised manuscript, we have removed all assertions of a "metabolism-independent" mechanism. Instead, we focus on demonstrating that nuclear-localized IDH1 contributes to chromatin state regulation during terminal erythropoiesis (e.g., H3K79me3 accumulation). While we acknowledge that nuclear IDH1’s enzymatic activity may still play a role [12], our data emphasize its spatial association with chromatin remodeling. We now explicitly state that nuclear IDH1’s function may involve both enzymatic and structural roles, and further studies are required to dissect these mechanisms.
Reference:
(12) Kafkia E, Andres-Pons A, Ganter K, Seiler M, Smith TS, et al.Operation of a TCA cycle subnetwork in the mammalian nucleus. Sci Adv. 2022;8(35):eabq5206.
(2) It is not clear how the enrichment of H3K9me3, a prominent marker of heterochromatin, upon IDH1 knockdown in the primary erythroid culture (Figure 4), goes along with a 2-3-fold increase in euchromatin. Furthermore, in the immunofluorescence (IF) experiments presented in Figure 4Db, it seems that H3K9me3 levels decrease in intensity (the signal seems more diffuse), which seems to contrast the ChIP-seq data. It would be interesting to test for localization of other heterochromatin marks such as HP1gamma. As a related point, it is not clear at what stage of erythroid differentiation the ATAC-seq was performed upon luciferase- and IDH1-shRNA-mediated knockdown shown in Figure 6. If it was done at a similar stage (Day 15) as the electron microscopy in Figure 4B, then the authors should explain the discrepancy between the vast increase in euchromatin and the rather small increase in ATAC-seq signal upon IDH1 knockdown.
Thank you for raising this important point. We agree that while H3K9me3 and H3K27me2 modifications are detectable in the nucleus, their functional association with chromatin in this context remains unclear. Our ChIP-seq data did not reveal distinct enrichment peaks for H3K9me3 or H3K27me2 (unlike the well-defined H3K79me3 peaks), suggesting that these marks may not be stably bound to specific chromatin regions under the experimental conditions tested. However, we acknowledge that the absence of clear peaks in our dataset does not definitively rule out chromatin interactions, as technical limitations or transient binding dynamics could influence these results. To avoid over-interpretation, we have removed speculative statements about the chromatin-unbound status of H3K9me3 and H3K27me2 from the revised manuscript. This revision aligns with our broader effort to present conclusions strictly supported by the current data while highlighting open questions for future investigation.
(3)The subcellular localization of IDH1, in particular its presence on chromatin, is not convincing in light of histone H3 being enriched in the cytoplasm on the same Western blot. H3 would be expected to be mostly localized to the chromatin fraction (see, e.g., PMID: 31408165 that the authors cite). The same issue is seen in Figure 4A.
We sincerely appreciate the reviewer's insightful comment regarding the subcellular distribution of histone H3 in our study. We agree that histone H3 is classically associated with chromatin-bound fractions, and its cytoplasmic enrichment in our Western blot analyses appears counterintuitive at first glance. However, this observation is fully consistent with the unique biology of terminal erythroid differentiation, which involves drastic nuclear remodeling and histone release - a hallmark of terminal stage erythropoiesis. Terminal erythroid differentiation is characterized by progressive nuclear condensation, chromatin compaction, and eventual enucleation. During this phase, global chromatin reorganization leads to the active eviction of histones from the condensed nucleus into the cytoplasm. This process has been extensively documented in erythroid cells, with studies demonstrating cytoplasmic accumulation of histones H3 and H4 as a direct consequence of nuclear envelope breakdown and chromatin decondensation preceding enucleation [13-16]. Our experiments specifically analyzed terminal-stage polychromatic and orthochromatic erythroblasts. At this stage, histone releasing into the cytoplasm is a dominant biological event, explaining the pronounced cytoplasmic H3 signal in our subcellular fractionation assays.
In summary, the cytoplasmic enrichment of histone H3 in our data aligns with established principles of erythroid biology and reinforces the physiological relevance of our findings. We thank the reviewer for raising this critical point, which allowed us to better articulate the unique aspects of our experimental system.
Reference:
(13) Hattangadi SM, Martinez-Morilla S, Patterson HC, Shi J, Burke K, et al. Histones to the cytosol: exportin 7 is essential for normal terminal erythroid nuclear maturation. Blood. 2014;124(12):1931-1940.
(14) Zhao B, Mei Y, Schipma MJ, Roth EW, Bleher R, et al. Nuclear Condensation during Mouse Erythropoiesis Requires Caspase-3-Mediated Nuclear Opening. Dev Cell. 2016;36(5): 498-510.
(15) Zhao B, Liu H, Mei Y, Liu Y, Han X, et al. Disruption of erythroid nuclear opening and histone release in myelodysplastic syndromes. Cancer Med. 2019;8(3):1169-1174.
(16) Zhen R, Moo C, Zhao Z, Chen M, Feng H, et al. Wdr26 regulates nuclear condensation in developing erythroblasts. Blood. 2020;135(3):208-219.
(4) This manuscript will highly benefit from more precise and complete explanations of the experiments performed, the material and methods used, and the results presented. At times, the wording is confusing. As an example, one of the "Key points" is described as "Dyserythropoiesis is caused by downregulation of SIRT1 induced by H3K79me3 accumulation." It should probably read "upregulation of SIRT1".
We sincerely thank the reviewer for highlighting the need for improved clarity in our experimental descriptions and textual precision. We fully agree that rigorous wording is essential to accurately convey scientific findings. Specific modifications have been made and are highlighted in Track Changes mode in the resubmitted manuscript.
The reviewer correctly identified an inconsistency in the original phrasing of one key finding. The sentence in question ("Dyserythropoiesis is caused by downregulation of SIRT1 induced by H3K79me3 accumulation") has been revised to:"Dyserythropoiesis is caused by the upregulation of SIRT1 mediated through H3K79me3 accumulation." This correction aligns with our experimental data showing that H3K79me3 elevation promotes SIRT1 transcriptional activation. We apologize for this oversight and have verified the consistency of all regulatory claims in the text.
Recommendations for the authors:
Reviewer #1 (Recommendations For The Authors):
(1) It will be helpful to mention/introduce the cells used for the study at the beginning of the results section. For example, for Figure 1A neither the figure legend nor the results text includes information on the cells used.
Thanks for the reviewer’s suggestion. The detail information of the cells that were used in our study have been provided in the revised manuscript.
(2) Important details for many figures are lacking. For example, in Figure 5, there is no mention of the replicates for ChIP-Seq studies. Also, the criteria used for quantifications of abnormal nuclei, % euchromatin vs heterochromatin, the numbers of biological replicates, and how many fields/cells were used for these quantifications are missing.
We thank the reviewer for emphasizing the importance of methodological transparency. It has been revised accordingly. The ChIP-Seq data in Figure 5 was generated from three independent biological replicates to ensure reproducibility. In this study, Image J software was used to calculate the area of nuclear, heterochromatin/euchromatin and to quantify the percentage of euchromatin and heterochromatin. A minimum of 300 cells per group were evaluated, and the proportion of aberrant nuclei was calculated as (number of abnormal cells / total counted cells) × 100%.
(3) It will be helpful if supplemental data are ordered according to how they are discussed in the text. Currently, the order of the supplemental data is hard to keep track of eg., the results section starts describing supplemental Figure 1, then the text jumps to supplemental Figure 5 followed by Supplemental Figure 3 (and so on).
Thanks for the reviewer’s suggestion. It has been revised accordingly.
(4) Overall, there are many incomplete sentences and typos throughout the manuscript including some of the figures e.g. on page 10 the sentence "Since the generation of erythroid with abnormal nucleus and reduction of mature red blood cells caused by IDH1 absence are notable characteristics of MDS and AML." is incomplete. On page 11, it reads "Histone post-modifications". This needs to be either histone modifications or histone post-translational modifications. In Figure 4C, the y-axis title is hard to understand "% of euchromatin and heterochromatin". Overall, the document needs to be proofread and revised carefully.
Thanks for the reviewer’s suggestion. We have made revision accordingly in the revised manuscript. The sentence "Since the generation of erythroid with abnormal nucleus and reduction of mature red blood cells caused by IDH1 absence are notable characteristics of MDS and AML." has been revised to “The production of erythrocytes with abnormal nuclei and the reduction of mature erythrocytes due to IDH1 deletion are prominent features of MDS and AML.” “% of euchromatin and heterochromatin” has been modified to “Area ratio of euchromatin to heterochromatin”.
Reviewer #3 (Recommendations For The Authors):
The following critique points aim to help the authors to improve their manuscript:
(1) The authors reason (p. 10) that because mutant IDH1 has been shown to result in altered chromatin organization, this could be the case in their system, too. However, mutant IDH1 has an ascribed metabolic consequence, the generation of 2-HG, which further weakens the author's argument for an enzymatically independent role of IDH1 in their system. The same is true for the author's observation in Supplementary Figure 9B that in IDH1-mutant AML/MDS samples, H3K79me3 colocalized with the IDH1 mutants in the nucleus. Again, this speaks in favor of IDH1's role being linked to metabolism. The authors could re-write this manuscript, not so much emphasizing the separation of function between different subcellular forms of IDH1 but rather focusing on the chromatin changes and how they could be linked to the actual phenotype, the nuclear condensation and enucleation defect - if so, addressing the surprising finding of enrichment of both active and repressive chromatin marks will be important.
Thanks for the reviewer’s suggestion. We agree with the reviewers and editors all the data we present in the current are not robust enough to rigorously distinguish between enzymatic and enzymatic-independent roles of IDH1. In our revised manuscript, we have removed all assertions of a "metabolism-independent" mechanism. Instead, we focus on demonstrating that nuclear-localized IDH1 contributes to chromatin state regulation during terminal erythropoiesis (e.g., H3K79me3 accumulation).
(2) How come so many genes were downregulated by RNA-seq (about an equal number as upregulated genes) but not more open by ATAC-seq? The authors should discuss this result.
Thanks for the reviewer's suggestion. ATAC-seq showed an increase in chromatin accessibility after IDH1 deletion, but the number of up-regulated genes was slightly larger than that of down-regulated genes, which may be caused by the metabolic changes affected by IDH1 deletion. In order to explore the effect of chromatin accessibility changes on gene expression after IDH1 deletion, we analyzed the changes in differential gene expression at the differential ATAC peak region (as shown in the figure below), and the results showed that the gene expression at the ATAC peak region with increased chromatin accessibility was significantly up-regulated. This may explain the regulation of chromatin accessibility on gene expression.
(3) For the ChIP-seq analyses of H3K79me3, H3K27me2, and H3K9me3, the authors should not just show genome-wide data but also several example gene tracks to demonstrate the differential abundance of peaks in control versus IDH1 knockdown. Furthermore, the heatmap shown in Figure 5A should include broader regions spanning the gene bodies, to visualize the intergenic H3K27me2 and H3K9me3 peaks. Expression could very well be regulated from these intergenic regions as they could bear enhancer regions. ChIP-seq for H3K27Ac in the same setting would be very useful to identify those enhancers.
Thanks for the reviewer’s suggestion. It has been revised accordingly. We reanalyzed the ChIP-seq peak signal of H3K79me3, H3K27me2 and H3K9me3 in a wider region (±5Kb) at gene body, and the results showed that the H3K27me2 and H3K9me3 peak signals did not change significantly. Since H3K79me3 showed a higher peak signal and was mainly enriched in the promoter region, our subsequent analysis focusing on the impact of H3K79me3 accumulation on chromatin accessibility and gene expression might be more valuable.
Author response image 3.
ChIP-seq analysis show that the peak signal of H3K79me3,H3K27me2 and H3K9me3. (A) Heatmaps displayed normalized ChIP signal of H3K9me3, H3K27me2, and H3K79me3 at gene body regions. The window represents ±5 kb regions from the gene body. TES, transcriptional end site; TSS, transcriptional start site. (B) Representative peaks chart image showed normalized ChIP signal of H3K9me3, H3K27me2, and H3K79me3 at gene body regions.
(4) The absent or very mild delay (also no significance visible in the quantification plots) in the generation of orthochromatic erythroblasts on Day 13 upon IDH1 shRNA knockdown as per a4-integrin/Band3 flow cytometry does not correspond to the already quite prominent number of multinucleated cells at that stage seen by cytospin/Giemsa staining. Why do the authors think this is the case? Cytospin/Giemsa staining might be the better method to quantify this phenotype and the authors should quantify the cells at different stages in at least 100 cells from non-overlapping cytospin images.
Thanks for the reviewer’s suggestion. We have supplemented the cytpspin assay and the results were presented in Supplemental Figure 4.
(5) The pull-down assay in Figure 7E does not show a specific binding of H3K79me3 to the SIRT1 promoter. Rather, there is just more H3K79me3 in the nucleus, thus leading to generally increased binding. The authors should show that H3K79me3 does not bind more just everywhere but to specific loci. The ChIP-seq data mention only categories but don't show any gene lists that could hint at the specificity of H3K79me3 binding at genes that would promote nuclear abnormalities and enucleation defects.
We thank the reviewer for pointing this out. The GSEA results of H3K79me3 peak showed enrichment of chromatin related biological processes, and the list of associated genes is shown Figure 7B. In addition, we also displayed the changes in H3K79me3 peak signals, ATAC peak signals, and gene expression at gene loci of three chromatin-associated genes (SIRT1, KMT5A and NUCKS1).
(6) P. 12: "Representatively, gene expression levels and ATAC peak signals at SIRT1 locus were elevated in IDH1-shRNA group and were accompanied by enrichment of H3K9me3 (Figure 7F)." Figure 7F does not show an enrichment of H3K9me3, but if the authors found such, they should explain how this modification correlates with the activation of gene expression.
Thank you for bringing this issue to our attention. We sincerely apologize for the mistake in the description of Figure 7F on page 12. We have already corrected this error in the revised manuscript.
(7) Related to the mild phenotype by flow cytometry on Day 13, are the "3 independent biological replicates" from culturing and differentiating CD34 cells from 3 different donors? If all are from the same donor, experiments from at least a second donor should be performed to generalize the results.
In our current study, CD34<sup>+</sup> cells were derived from different donors.
(8) If the images in Supplementary Figure 4 are only the indicated cell type, then it is not clear how the data were quantified since only some cells in each image are pointed at and others do not seem to have as large nuclei. There is also no explanation in the legend what the colors mean (nuclei were presumably stained with DAPI, not clear what the cytoplasm stain is - GPA?).
We thank the reviewer for pointing this out. We have revised the manuscript accordingly. Specifically, the nuclei was stained with DAPI and the color was blue. The cell membrane was stained with GPA and the color was red. This staining method allows for clear visualization of the cell structure and helps to better understand the localization of the proteins of interest.
(9) It is not clear to this reviewer whether Figure 4F is a quantification of the Western Blot or of the IF data.
Figure 4F is a quantification of the Western Blot experiment.
(10) The authors sometimes do not describe experiments well, e.g., "treatment of IDH1-deficient erythroid cells with IDH1-EX527" (p. 13). EX-527 is a SIRT1 inhibitor, which the authors only explicitly mention later in that paragraph. It is unclear to this reviewer, why the authors call it IDH1-EX527.
Thank you for pointing out the unclear description in our manuscript. We apologize for the confusion caused by the unclear statement. We have revised the manuscript accordingly. The compound EX-527 is a SIRT1 inhibitor, and we have corrected the description to simply "EX-527" in the revised manuscript.
(11) The end of the introduction needs revising to be more concise; the last paragraph on p. 4 ("Recently, the decreased expression of IDH1...") partially should be integrated with the previous paragraph, and partially is repeated in the last paragraph (top paragraph on p. 5). The last sentence on p. 4, "These findings strongly suggest that aberrant expression of IDH1 is also an important factor in the pathogenesis of AML and MDS.", should rather read "increased expression of IDH1", to distinguish it from mutant IDH1 (mutant IDH1 is also aberrantly expressed IDH1).
We appreciated the reviewer for the helpful suggestion. Considering that the inclusion of this paragraph did not provide a valuable contribution to the formulation of the scientific question, we have removed it after careful consideration, and the revised manuscript is generally more logically smooth.
(12) Abstract and last sentence of the introduction: "innovative perspective" should be re-worded, as the authors present data, not a perspective. Maybe could use "evidence".
Thanks for the reviewer’s suggestion. It has been revised accordingly.
(13) "IDH1-mut AML/MDS" on p. 11. The authors should provide more information about these AML/MDS samples. The legend contains no information about them/their mutational status. How many samples did the authors look at? Do these cells contain mutations other than IDH1?
Thanks for the reviewer’s suggestion. The detail information of these AML/MDS samples are provide in supplemental table 1. In our current study, we collected ten AML/MDS samples and the majority of the samples only contain IDH1 mutations at different sites.
(14) The statement, "Taken together, these results indicated that IDH1 deficiency reshaped chromatin states and subsequently altered gene expression pattern, especially for genes regulated by H3K79me3, which was the mechanism underlying roles of IDH1 in modulation of terminal erythropoiesis." (p. 10), is not correct at that point in the manuscript as the authors have not yet introduced the RNA-seq data.
Thanks for the reviewer’s suggestion. The statement has been revised to “Taken together, these results indicated that IDH1 deficiency reshaped chromatin states by altering the abundance and distribution of H3K79me3, which was the mechanism underlying roles of IDH1 in modulation of terminal erythropoiesis”.
(15) For easier readability, the authors should present the data in order. For example, the supplemental data for IDH shRNA and siRNA should be presented together and not in Supplementary Figures 1 and 5. Supplementary Figure 3 is mentioned after Supplementary Figure 1, but before Supplementary Figure 2 - again, all data need to be presented in subsequent figures to be viewed together.
Thank you for your suggestion regarding the order of data presentation. We have reorganized the figures in the manuscript to improve readability. We apologize for any confusion caused by the previous arrangement and hope that the revised version meets your expectations.
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Author response:
Reviewer #1:
The manuscript Xu et al. explores the regulation of the microtubule minus end protein CAMSAP2 localization to the Golgi by the Serine/threonine-protein kinase MARK2 (PAR1, PAR1B). The authors utilize immunofluorescence and biochemical approaches to demonstrate that MARK2 is localized at the Golgi apparatus via its spacer domain. They show that depletion of this protein alters Golgi morphology and diminishes CAMSAP2 localization to the Golgi apparatus. The authors combine mass spectroscopy and immunoprecipitation to show that CAMSAP2 is phosphorylated at S835 by MARK2, and that this phosphorylation regulates localization of CAMSAP2 at Golgi membranes. Further, the authors identify USO1 (p115) as the Golgi resident protein mediating CAMSAP2 recruitment to the Golgi apparatus following S835 phosphorylation. The authors would need to address the following queries to support their conclusions.
We sincerely thank the reviewer for their valuable time and effort in evaluating our manuscript. We deeply appreciate the constructive feedback and insightful suggestions, which have been instrumental in improving the quality and clarity of our study. We have carefully considered all the comments and have made the necessary revisions to address the concerns raised.
Major Comments
(1) Dynamic localization of CAMSAP2 during Golgi reorientation
- The authors use fixed wound edges assays and co-localization analysis to describe changes in CAMSAP2 positioning during Golgi reorientation in response to polarizing cues (a free wound edge in this case). In Figure 1C, they present a graphical representation of quantified immunofluorescence images, using color coding to to describe the three states of Golgi reorientation in response to a wound (green, blue, red indicating non-polarised, partial and complete Golgi reorientation, respectively). They then use these 'colour coded' classifications to quantitate CAMSAP2/GM130 co-localization.It is unclear why the authors have not just used representative immunofluorescence images in the main figures. Transparent, color overlays could be placed over the cells in the representative images to indicate which of the three described states each cell is currently exhibiting. However, for clarity, I would recommend changing the color coded 'states' to a descriptor rather than a color. i.e. Figure 1D x axis labels should be 'complete' and 'partial', instead of 'red' and 'blue'.
Thank you for this insightful suggestion. We have added representative immunofluorescence images with transparent color overlay to indicate the three Golgi orientation states. These images are included in Supplementary Figure 2B-C, providing a clear visual reference for the quantitative data. Additionally, we have revised the x-axis labels in Figure 1E from "Red" and "Blue" to "Complete" and "Partial" to ensure clarity and consistency with the descriptive terminology in the text. These changes are described in the Results section (page 7, lines 15-19) and the figure legend (page 29, lines 27-29).
We believe these updates improve the clarity and accessibility of our figures and hope they address the reviewer’s concerns.
- note- figure 2 F-G, is semi quantitative, why did the authors not just measure Golgi angle using the nucleus and Golgi distribution?
We appreciate the reviewer’s comment on this point. Following the recommendation, we have performed an additional analysis measuring Golgi orientation angles based on the nucleus-Golgi distribution. This quantitative approach complements our initial semi-quantitative analysis and provides a more precise assessment of Golgi orientation during cell migration.
The new data have been incorporated into Supplementary Figure 1F-H. These results clearly demonstrate the consistency between the quantitative and semi-quantitative methods, further validating our findings and highlighting the dynamic changes in Golgi orientation during cell migration. These changes are described in the Results section (page 6, lines 24-31).
- While it is established that the Golgi is dispersed during reorientation in wound edge migration, the Golgi apparatus also becomes dispersed/less condensed prior to cell division. As the authors have used fixed images - how are they sure that the Golgi morphology or CAMSAP2 localization in 'blue cells' are indicative of Golgi reorientation and not division? Live imaging of cells expressing CAMSAP2, and an additional Golgi marker could be used to demonstrate that the described changes in Golgi morphology and CAMSAP2 localization are occurring during the rear-to-front transition of the Golgi.
Thank you for raising this important question. To address this concern, we carefully examined the nuclear morphology of dispersed Golgi cells and found no evidence of mitotic features, indicating that these cells are not undergoing division (Figure 1A, Supplemental Figure 2A). Furthermore, during the scratch wound assay, we use 2% serum to culture the cells, which helps minimize the impact of cell division. This analysis has been added to the Results section (page7, lines 19-22 in the revised manuscript).
Additionally, we conducted live-cell imaging, as suggested, using cells expressing a Golgi marker. This approach confirmed that Golgi dispersion occurs transiently during reorientation in cell migration. The new live-cell imaging data have been incorporated into Supplementary Figure 2A, and the corresponding description has been updated in the Results section (page 7, lines 2-5).
Finally, considering that overexpression of CAMSAP2 can lead to artifactually condensed Golgi structures, we used endogenous staining to observe CAMSAP2 localization at different stages of migration. These observations provide a clearer understanding of CAMSAP2 dynamics during Golgi reorientation and are now presented in revised Figure 1A-B. This information has been described in the Results section (page 7, lines 5-10).
We hope these additions and clarifications address the reviewer’s concerns. Once again, we are deeply grateful for this constructive feedback, which has greatly improved the robustness of our study.
(2) MARK2 localization to the Golgi apparatus
- The authors investigated the positioning of endogenous MARK2 via immunofluorescence staining, and exogenous flag-tagged MARK2 in a KO background. The description of the protocol required to visualize Golgi localization of MARK2 is inconsistent between the results and methods text. The results text reads as through the 2% serum incubation occurs as a blocking step following fixation. Conversely, the methods section describes the 2% serum incubation as occurring just prior to fixation as a form of serum starvation. The authors need to clarify which of these protocols is correct. Further, whilst I can appreciate that the mechanistic understanding of why serum starvation is required for MARK2 Golgi localization is beyond the scope of the current work, the authors should at a minimum speculate in the discussion as to why they think it might occur.
We sincerely thank the reviewer for the constructive feedback on the localization of MARK2 at the Golgi. Due to the complexity and variability of this phenomenon, we decided to remove the related data from the current manuscript to maintain the rigor of our study. However, we have included a discussion of this phenomenon in the Discussion section (page 13, lines 31-39 and page 14, 1-6in the revised manuscript) and plan to further investigate it in future studies.
The localization of MARK2 at the Golgi was initially observed in experiments following serum starvation, where cells were fixed and stained (The data is not displayed). This observation was supported by the loss of Golgi localization in MARK2 knockdown cells, indicating the specificity of the antibody (The data is not displayed). However, this phenomenon was not consistently observed across all cells, likely due to its transient nature.We speculate that the localization of MARK2 to the Golgi depends on its activity and post-translational modifications. For example, phosphorylation at T595 has been reported to regulate the translocation of MARK2 from the plasma membrane to the cytoplasm (Hurov et al., 2004). Serum starvation might induce modifications or conformational changes in MARK2, leading to its temporary Golgi localization. Additionally, we hypothesize that this localization may coincide with specific Golgi dynamics, such as the transition from dispersed to ribbon-like structures during cell migration.
We also acknowledge the inconsistency in the Results and Methods sections regarding serum starvation. We confirm that serum starvation was performed prior to fixation as an experimental condition, rather than as a blocking step in immunostaining. This clarification has been incorporated into the revised Methods section (page 24, lines 11-12).
We hope this clarification, along with our planned future studies, adequately addresses the reviewer’s concerns. Once again, we deeply appreciate the reviewer’s valuable comments, which have provided important insights for our ongoing work. References:
Hurov, J.B., Watkins, J.L., and Piwnica-Worms, H. (2004). Atypical PKC phosphorylates PAR-1 kinases to regulate localization and activity. Curr Biol 14 (8): 736-741.
- The authors should strengthen their findings by using validated tools/methods consistent with previous publications. i.e. Waterman lab has published two MARK2 constructs- Apple and eGFP tagged versions (doi.org/10.1016/j.cub.2022.04.088), and the localization of MARK2 in U2Os cells (using the same antibody (Anti- MARK2 C-terminal, ABCAM Cat# ab136872). The authors should (1) image the cells live using eGFP-tagged MARK2 during serum starvation to show the dynamics of this localization, (2) image U2Os cells using the abcam ab136872 antibody +/- 2% serum starve. Two MARK2 antibodies are listed in Table 2. Does abcam (ab133724) show a similar localisation?
- The Golgi localization of MARK2 occurs in the absence of the T structural domain, but not when full length MARK2 is expressed. The authors conclude the T- domain is likely inhibitory. When combined with the requirement for serum starvation for this interaction to occur, the authors should clarify the physiological relevance of these observations.
We sincerely thank the reviewer for their valuable suggestions regarding the use of tools and methods and the physiological relevance of MARK2 localization to the Golgi. Regarding the question of how MARK2 itself localizes to the Golgi, we are currently unable to fully elucidate the underlying mechanism. Therefore, we have removed the discussion of MARK2’s Golgi localization from the manuscript to ensure scientific accuracy. However, Below, we provide our detailed response as soon as possible:
First, regarding the suggestion to use tools and methods developed by the Waterman lab to strengthen our findings, we have carefully evaluated their applicability. In our live-cell imaging experiments, we found that full-length MARK2 does not stably localize to the Golgi, even under serum starvation conditions. However, truncated MARK2 mutants lacking the Tail (T) domain exhibit robust Golgi localization. Furthermore, our immunofluorescence staining results indicate that the Spacer domain is the minimal region required for MARK2 localization at the Golgi. Based on these findings, we believe that live-cell imaging of EGFP-tagged full-length MARK2 may not effectively reveal the dynamics of its Golgi localization. However, we plan to focus on the truncated constructs in future studies to better explore the mechanisms underlying MARK2's dynamic behavior.
Regarding the use of the ab136872 antibody to stain U2OS cells with and without serum starvation, we note that the protocol described by the Waterman lab involves pre-fixation and permeabilization steps, which are not compatible with live-cell imaging. Additionally, we observed that MARK2 Golgi localization appears to be condition-dependent and may coincide with specific Golgi dynamics, such as transitions from dispersed stacks to intact ribbon structures. These events are likely brief and challenging to capture consistently. Nevertheless, we recognize the value of this experimental design and plan to adapt the staining conditions in future work to validate our results further. As for the ab133724 antibody listed in Table 2, we clarify that it has only been validated for Western blotting in our study and does not yield reliable results in immunofluorescence experiments. For this reason, all immunofluorescence staining in this study relied exclusively on ab136872. This distinction has been clarified in the revised Table 2 .
Regarding the hypothesis that the Tail domain of MARK2 is inhibitory, our observations showed that truncated MARK2 mutants lacking the T domain stably localized to the Golgi, whereas fulllength MARK2 did not. Literature evidence supports this hypothesis, as studies on the yeast homolog Kin2 indicate that the C-terminal region (including the Tail domain) binds to the Nterminal catalytic domain to inhibit kinase activity (Elbert et al., 2005). We speculate that serum starvation disrupts this intramolecular interaction, relieving the inhibition by the T domain, activating MARK2, and promoting its localization to the Golgi. Moreover, we hypothesize that the transient nature of MARK2 localization to the Golgi may be related to specific Golgi remodeling processes, such as the transition from dispersed stacks to intact ribbon structures during cell migration or polarity establishment.
References:
Elbert, M., Rossi, G., and Brennwald, P. (2005). The yeast par-1 homologs kin1 and kin2 show genetic and physical interactions with components of the exocytic machinery. Mol Biol Cell 16 (2): 532-549.
(3) Phosphorylation of CAMSAP2 by MARK2
- The authors examined the effects of MARK2 phosphorylation of CAMSAP2 on Golgi architecture through expression of WT-CAMSAP2 and two CAMSAP2 S835 mutants in CAMSAP2 KO cells. They find that CAMSAP2 S835A (non-phosphorylatable) was less capable of rescuing Golgi morphology than CAMSAP2 S835D (phosphomimetic). Golgi area has been measured to demonstrate this phenomenon. Representative immunofluorescence images in Fig. 4D appear to indicate that this is the case. However, quantification in Fig. 4E does not show significance between HA-CAMSAP2 and HA-CAMSAP2A that would support the initial claim. The authors could analyze other aspects of Golgi morphology (e.g. number of Golgi fragments, degree of dispersal around the nucleus) to capture the clear structural defects demonstrated in HACAMSAP2A cells.
We sincerely thank the reviewer for their valuable feedback and for pointing out potential areas of improvement in our analysis of Golgi morphology. We apologize for any misunderstanding caused by our description of the results in Figure 4E.
The quantification indeed shows a significant difference between HA-CAMSAP2 and HACAMSAP2A in terms of Golgi area, as indicated in the figure by the statistical annotations (pvalue provided in the legend). To ensure clarity, we have revised the figure legend (page 32, lines 19-23 in the revised manuscript) to explicitly describe the statistical significance, and the method used for quantification.
Because the quantification indeed shows a significant difference between HA-CAMSAP2 and HA-CAMSAP2A in terms of Golgi area, and to maintain consistency throughout the manuscript, we did not further analyze other aspects of Golgi morphology.
We hope this clarification, along with the additional analyses, will address the reviewer’s concerns. Once again, we are deeply grateful for these constructive comments, which have helped us improve the quality and robustness of our study.
- Wound edge assays are used to capture the difference in Golgi reorientation towards the leading edge between CAMSAP2 S835A and CAMSAP2 S835D. However, these studies lack comparison to WT-CAMSAP2 that would support the role of phosphorylated CAMSAP2 in reorienting the Golgi in this context.
We sincerely thank the reviewer for their insightful suggestion. In response, we have added a comparison between CAMSAP2 S835A/D and WT-CAMSAP2, in addition to HT1080 and MARK2 KO cells, to better evaluate the role of phosphorylated CAMSAP2 in Golgi reorientation.
The results, now shown in Figure 5A-C, indicate that in the absence of MARK2, there is no significant difference in Golgi reorientation between WT-CAMSAP2 and CAMSAP2 S835A. This observation supports the conclusion that MARK2-mediated phosphorylation of CAMSAP2 at S835 is essential for effective Golgi reorientation.
To enhance clarity, we have updated the corresponding Results section (page 9, lines 37-40 and page 10, line 1 in the revised manuscript) to describe this additional comparison. We believe this analysis strengthens our findings and provides a clearer understanding of the role of phosphorylated CAMSAP2 in Golgi dynamics.
We hope this additional data addresses the reviewer’s concerns. Once again, we are grateful for the constructive feedback, which has helped improve the clarity and robustness of our study.
(4) Identification of CAMSAP2 interaction partners
- Quantification of interaction ability between CAMSAP2 and CG-NAP, CLASP2, or USO1 in Fig. 5D, 5F and 5J respectively, lack WT-CAMSAP2 comparisons.
We sincerely thank the reviewer for their valuable suggestion. In response, we have included WT-CAMSAP2 data in the quantification of interaction ability between CAMSAP2 and CG-NAP, CLASP2, and USO1. These results, now shown in revised Figures 5 D-G and Figures 6 C-D, provide a direct comparison that further validates the differential interaction abilities of CAMSAP2 mutants.
The inclusion of WT-CAMSAP2 allows us to better contextualize the effects of specific mutations on CAMSAP2 interactions and strengthens our conclusions regarding the role of these interactions in Golgi dynamics.
We hope this addition addresses the reviewer’s concerns and enhances the clarity and robustness of our study. We deeply appreciate the constructive feedback, which has been instrumental in improving our manuscript.
- The CG-NAP immunoblot presented in Fig. 5C shows that the protein is 310 kDa, which is the incorrect molecular weight. CG-NAP (AKAP450) should appear at around 450 kDa. Further, no CG-NAP antibody is included in Table 2 - Information of Antibodies. The authors need to explain this discrepancy.
We sincerely apologize for the lack of clarity in our annotation and description, which may have caused confusion regarding the CG-NAP immunoblot presented in Figure 5C (Figure 5D in the revised manuscript). To clarify, CG-NAP (AKAP450) is indeed a 450 kDa protein, and the marker at 310 kDa represents the molecular weight marker’s upper limit, above which CG-NAP is observed. This has been clarified in the figure legend (page 33, lines 21-23 in the revised manuscript).
Regarding the CG-NAP antibody, it was custom-made and purified in our laboratory. Polyclonal antisera against CG-NAP, designated as αEE, were generated by immunizing rabbits with GSTfused fragments of CG-NAP (aa 423–542). This antibody has been validated extensively in our previous research, demonstrating its specificity and reliability (Wang et al., 2017). The details of the antibody preparation are included in the footnote of Table 2 for reference.
We hope this clarification, along with the additional context regarding the antibody validation, resolves the reviewer’s concerns. We are deeply grateful for the reviewer’s attention to detail, which has helped us improve the clarity and rigor of our manuscript.
References:
Wang, J., Xu, H., Jiang, Y., Takahashi, M., Takeichi, M., and Meng, W. (2017). CAMSAP3dependent microtubule dynamics regulates Golgi assembly in epithelial cells. Journal of genetics and genomics = Yi chuan xue bao 44 (1): 39-49.
Minor Comments
- Authors should change immunofluorescence images to colorblind friendly colors. The current presentation of merged overlays makes it really difficult to interpret- I would strongly encourage inverted or at a minimum greyscale individual images of key proteins of interest.
We sincerely thank the reviewer for their valuable suggestion regarding the presentation of immunofluorescence images. In response, we have converted the images in Figure 1C to greyscale individual images for each key protein of interest. This adjustment ensures that the figures are more accessible and interpretable, including for readers with color vision deficiencies.
We hope this modification addresses the reviewer’s concern and improves the clarity of our data presentation. We are grateful for the constructive feedback, which has helped us enhance the overall quality of our figures.
- On p. 8 text should be amended to 'Previous literature has documented MARK2's localization to the microtubules, microtubule-organizing center (MTOC), focal adhesions..'
We sincerely thank the reviewer for their comment regarding the text on page 8. Considering the reasoning provided in response to question 2, where we clarified that MARK2's Golgi localization is not fully understood, we have decided to remove this section from the manuscript to maintain the accuracy and rigor of our study.
We appreciate the reviewer’s attention to detail and constructive feedback, which has helped us improve the clarity and focus of our manuscript.
- In Fig.1A scale bars are not shown on individual channel images of CAMSAP or GM130
We sincerely thank the reviewer for pointing out the omission of scale bars in the individual channel images of CAMSAP and GM130 in Figure 1A (Figure 1C in the revised manuscript). In response, we have added a scale bar (5 μm) to the CAMSAP2 channel, as shown in the revised Figure 1C. These updates have been described in the figure legend (page 29, line 21).
We hope this modification addresses the reviewer’s concern and improves the accuracy and clarity of our figure presentation. We greatly appreciate the reviewer’s constructive feedback, which has helped enhance the quality of our manuscript.
- In Fig. 1B the title should be amended to 'Colocalization of CAMSAP2/GM130'
We sincerely thank the reviewer for their suggestion to amend the title in Figure 1B (Figure 1D in the revised manuscript). In response, we have updated the title to "Colocalization of CAMSAP2/GM130," as shown in the revised Figure 1D.
We hope this modification addresses the reviewer’s concern and improves the clarity and accuracy of the figure. We greatly appreciate the reviewer’s valuable feedback, which has helped us refine the presentation of our results.
- In Fig. 2F, 5A, and Sup Fig 3C scale bars have been presented vertically
We sincerely thank the reviewer for pointing out the issue with the vertical orientation of scale bars in Figures 2F (Figure 2D in the revised manuscript), 5A, and Supplementary Figure 3C. In response, we have modified the scale bars in revised Figures 2D and 5A to a horizontal orientation for improved consistency and clarity. Additionally, Supplementary Figure 3C has been removed from the revised manuscript.
We hope these adjustments address the reviewer’s concerns and enhance the overall presentation quality of the figures. We greatly appreciate the reviewer’s constructive feedback, which has helped us refine our manuscript.
- Panels are not correctly aligned, and images are not evenly spaced or sized in multiple figures - Fig. 2F, 4D, Sup Fig. 1F, Sup Fig. 2C, Sup Fig. 3E, Sup Fig. 4C
We sincerely thank the reviewer for pointing out the misalignment and uneven spacing or sizing of panels in multiple figures, including Figures 2F, 4D, Supplementary Figures 1F, 2C, 3E, and 4C (Figure 2D, 4D, Supplementary Figures 1F, 2C, and 3H in the revised manuscript.
Supplementary Figure 3E was removed from our manuscript). In response, we have standardized the spacing and sizing of all panels throughout the manuscript to ensure consistency and improve visual clarity.
We hope this modification addresses the reviewer’s concerns and enhances the overall presentation quality of our figures. We greatly appreciate the reviewer’s constructive feedback, which has helped us improve the organization and professionalism of our manuscript.
- An uncolored additional data point is present in Fig. 3F
We sincerely thank the reviewer for pointing out the presence of an uncolored additional data point in Figure 3F. In response, we have removed this data point from the revised figure to ensure accuracy and clarity.
We hope this adjustment resolves the reviewer’s concern and improves the overall quality of the figure. We greatly appreciate the reviewer’s careful review and constructive feedback, which have helped us refine our manuscript.
- In Fig. 3A 'GAMSAP2/GM130' in the vertical axis label should be amended to 'CAMSAP2/GM130'
We sincerely thank the reviewer for pointing out the error in the vertical axis label of Figure 3A. In response, we have corrected "GAMSAP2/GM130" to "CAMSAP2/GM130," as shown in the revised Figure 3I.
We hope this correction resolves the reviewer’s concern and improves the accuracy of our figure. We greatly appreciate the reviewer’s careful review and constructive feedback, which have helped us refine our manuscript.
- In Fig 5A the green label should be amended to 'GFP-CAMSAP2' instead of 'GFP'
We sincerely apologize for the confusion caused by our labeling in Figure 5A. To clarify, the green label “GFP” refers to the antibody used, while “GFP-CAMSAP2” is indicated at the top of the figure to specify the construct being analyzed.
We hope this explanation resolves the misunderstanding and provides clarity regarding the labeling in Figure 5A. We greatly appreciate the reviewer’s feedback, which has allowed us to address this issue and improve the precision of our figure annotations.
- The repeated use of contractions throughout the manuscript was distracting, I would strongly encourage removing these.
We sincerely thank the reviewer for pointing out the distracting use of contractions in the manuscript. In response, we have removed and replaced all contractions with their full forms to improve the clarity and formal tone of the text.
We hope this modification addresses the reviewer’s concern and enhances the readability and professionalism of our manuscript. We greatly appreciate the reviewer’s constructive feedback, which has helped us refine the quality of our writing.
Reviewer #2:
Summary
This work by the Meng lab investigates the role of the proteins MARK2 and CAMSAP2 in the Golgi reorientation during cell polarisation and migration. They identified that both proteins interact together and that MARK2 phosphorylates CAMSAP2 on the residue S835. They show that the phosphorylation affects the localisation of CAMSAP2 at the Golgi apparatus and in turn influences the Golgi structure itself. Using the TurboID experimental approach, the author identified the USO1 protein as a protein that binds differentially to CAMSAP2 when it is itself phosphorylated at residue 835. Dissecting the molecular mechanisms controlling Golgi polarisation during cell migration is a highly complex but fundamental issue in cell biology and the author may have identified one important key step in this process. However, although the authors have made a genuine iconographic effort to help the reader understand their point of view, the data presented in this study appear sometimes fragile, lacking rigour in the analysis or over-interpreted. Additional analyses need to be conducted to strengthen this study and elevate it to the level it deserves.
We sincerely thank the reviewer for their thoughtful evaluation and recognition of our study's significance in understanding Golgi reorientation during cell migration. We appreciate the constructive feedback regarding data robustness, clarity, and interpretation. In response, we have conducted additional analyses, revised data presentation, and ensured cautious interpretation throughout the manuscript. These changes aim to address the reviewer’s concerns comprehensively and strengthen the scientific rigor of our study.
Major comments
In order to conclude as they do about the putative role of USO1, the authors need to perform a siRNA/CRISPR of USO1 to validate its role in anchoring CAMSAP2 to the Golgi apparatus in a MARK2 phosphorylation-dependent manner. In other words, does depletion of USO1 affect the recruitment of CAMSAP2 to the Golgi apparatus?
We sincerely thank the reviewer for their insightful suggestion regarding the role of USO1 in anchoring CAMSAP2 to the Golgi apparatus. In response, we performed USO1 knockdown using siRNA and quantified the Pearson correlation coefficient of CAMSAP2 and GM130 colocalization in control and USO1-knockdown cells.
The results show that CAMSAP2 localization to the Golgi is significantly reduced in USO1knockdown cells, confirming that USO1 plays a critical role in recruiting CAMSAP2 to the Golgi apparatus. These results are now presented in Figures 6 E–G, and corresponding updates have been incorporated into the Results section (page 10, lines 36-37 in the revised manuscript).
We hope this additional experiment addresses the reviewer’s concern and strengthens our conclusions regarding the role of USO1. We are grateful for the reviewer’s constructive feedback, which has greatly improved the robustness of our study.
It is not clear from this study exactly when and where MARK2 phosphorylates CAMSAP2. What is the result of overexpression of the two proteins in their respective localisation to the Golgi apparatus? As binding between CAMSAP2 and MARK2 appears robust in the immunoprecipitation assay, this should be readily investigated.
We sincerely thank the reviewer for their insightful comments and questions. To address the role of MARK2 in regulating CAMSAP2 localization to the Golgi apparatus, we overexpressed GFPMARK2 in cells and compared its effects on CAMSAP2 localization to the Golgi with control cells overexpressing GFP alone. Our results show that CAMSAP2 localization to the Golgi is significantly increased in GFP-MARK2-overexpressing cells, as shown in Supplementary Figures 3C and 3E. Corresponding updates have been incorporated into the Results section (page 8, lines 25-27 in the revised manuscript).
Regarding the question of how MARK2 itself localizes to the Golgi, we are currently unable to fully elucidate the underlying mechanism. Therefore, we have removed the discussion of MARK2’s Golgi localization from the manuscript to ensure scientific accuracy. Consequently, we have not conducted experiments to assess the effects of CAMSAP2 overexpression on MARK2’s localization to the Golgi.
We hope this explanation clarifies the reviewer’s concerns. We are grateful for the reviewer’s constructive feedback, which has guided us in improving the clarity and focus of our study.
To strengthen their results, can the author map the interaction domains between CAMSAP2 and MARK2? The authors have at their disposal all the constructs necessary for this dissection.
We sincerely thank the reviewer for their insightful suggestion to map the interaction domains between CAMSAP2 and MARK2. In response, we performed immunoprecipitation experiments using truncated constructs of CAMSAP2. Our results reveal that MARK2 interacts specifically with the C-terminus (1149F) of CAMSAP2, as shown in Supplementary Figures 3A and 3B. Corresponding updates have been incorporated into the Results section (page 7, lines 41-42 and page 8, line 1 in the revised manuscript).
We hope this additional analysis addresses the reviewer’s suggestion and further strengthens our conclusions. We greatly appreciate the reviewer’s constructive feedback, which has helped improve the depth of our study.
Minor comments
Sup-fig1
H: It is not clear if the polarisation experiment has been repeated three times (as it should) and pooled or is just the result of one experiment?
We sincerely apologize for the lack of clarity regarding the experimental details for Supplementary Figure 1H. To clarify, the polarization experiment was repeated three times, and the results were pooled to generate the data presented. We have updated the figure legend for Supplementary Figure 1H to explicitly state this information (page 35, lines 27-29 in the revised manuscript).
We hope this clarification resolves the reviewer’s concern. We greatly appreciate the reviewer’s careful review and constructive feedback, which have helped us improve the accuracy and transparency of our manuscript.
Sup-fig2
C: "Immunofluorescence staining plots" formula used in the legend is not clear. Which condition is presented in the panel, parental HT1080 or CAMSAP2 KO cells?
We thank the reviewer for pointing out the lack of clarity regarding the conditions presented in Supplementary Figure 2C. To clarify, the immunofluorescence staining plots shown in this panel are from parental HT1080 cells. We have updated the figure legend to include this information (page 36, line 14 in the revised manuscript).
We hope this clarification resolves the reviewer’s concern and improves the transparency of our data presentation. We greatly appreciate the reviewer’s feedback, which has helped us refine the manuscript.
Figure 1
D: In the plot, the colour of the points for the "red cells" are red but the one for the "blue cells" are green, this is confusing.
E: Once again, the colour choice is confusing as blue cells (t=0.5h) are quantified using red dots and red cells (t=2h) quantified using green dots. The t=0h condition should be quantified as well and added to the graph.
F: Representative CAMSAP2 immunofluorescence pictures for the three time points should be provided in addition to the drawings.
We thank the reviewer for their valuable comments regarding Figure 1D (revised Figure 1E), Figure 1E (revised Figure 1B), and Figure 1F (revised Supplementary Figure 2C).
- Figure 1D (revised Figure 1E): we have modified the x-axis labels and adjusted the color scheme of the data points to ensure consistency and avoid confusion.
- Figure 1E (revised Figure 1B): we have updated the x-axis and included the quantification of the t=0h condition, which has been added to the graph.
- Figure 1F (revised Supplementary Figure 2C): we have provided representative immunofluorescence images of CAMSAP2 for the three-time points to complement the schematic drawings.
We hope these revisions address the reviewer’s concerns and improve the clarity and completeness of our data presentation. We greatly appreciate the reviewer’s constructive feedback, which has significantly contributed to enhancing our manuscript.
Figure 2
A: No methodology in the material and methods is provided for this analysis.
B: Can the authors be more precise regarding the source of the CAMSAP2 interactants? Can the author provide the citation of the publication describing the CAMSAP2-MARK2 interaction?
D: Genotyping for the MARK2 KO cell line should be provided the same way it was provided for the CAMSAP2 cell line in Sup-fig1. "MARK2 was enriched around the Golgi apparatus in a significant proportion of HT1080 cells": which proportion of the cells?
F: The time point of fixation is missing
G: It is not clear if the polarisation experiment has been repeated three times (as it should) and pooled or is just the result of one experiment?
We thank the reviewer for their detailed comments and suggestions regarding Figure 2. Below, we provide clarifications and outline the modifications made:
- Figure 2A: The methodology for this analysis has been added to section 5.14 (Data statistics). Specifically, we have stated: “GO analysis of proteins was plotted using https://www.bioinformatics.com.cn, an online platform for data analysis and visualization” (page 26 lines 5-6 in the revised manuscript).
- Figure 2B: The CAMSAP2 interactants were derived from the study by Wu et al., 2016, which provides the source of these interactants. The interaction between CAMSAP2 and MARK2 is referenced from Zhou et al., 2020. These citations have been added to the relevant sections of the manuscript (page 30, lines 10-11 and 13-14).
- Figure 2D (removed in the revised manuscript): Genotyping for the MARK2 KO cell line has been provided in the same format as for the CAMSAP2 KO cell line in Figure 2G. Additionally, as the MARK2 Golgi localization discussion cannot yet be fully elucidated, we have removed this portion from the manuscript.
- Figure 2F (revised Figure 2D): The time point of fixation, which occurred 2 hours after the scratch wound assay, has been added to the figure legend (page 30, lines 15-16).
- Figure 2G (revised Figure 2E-F): The polarization experiment was repeated three times, and the results were pooled. This information has been included in the figure legend (page 30, lines 26 and 29).
We hope these updates address the reviewer’s concerns and improve the clarity and completeness of the manuscript. We are grateful for the reviewer’s constructive feedback, which has greatly enhanced the rigor of our study. References:
Wu, J., de Heus, C., Liu, Q., Bouchet, B.P., Noordstra, I., Jiang, K., Hua, S., Martin, M., Yang, C., Grigoriev, I., et al. (2016). Molecular Pathway of Microtubule Organization at the Golgi Apparatus. Dev Cell 39 (1): 44-60.
Sup-fig3
E: Although colocalisation between CAMSAP2 and MARK2 is clear in your serum conditions in HT1080 and RPE1 cells, the deletion domain analysis appears weak and insufficient to implicate the role of the spacer domain. This part should be deleted or strengthened, but the data do not satisfactorily support your conclusion as it stands.
We sincerely thank the reviewer for their critical comments regarding the deletion domain analysis of MARK2 and its role in colocalization with CAMSAP2. As the current data do not satisfactorily support our conclusions, we have removed all related content on MARK2 and the deletion domain analysis from the manuscript to maintain scientific rigor.
We appreciate the reviewer’s valuable feedback, which has helped us refine and improve the quality and focus of our study.
Figure 3
A: Can the reduced CAMSAP2 Golgi localisation phenotype be rescued by the overexpression of MARK2 cDNA in the MARK2 KO cells?
F: Presence of a white dot on the HT1080 plot
G: The composition of the homogenization buffer is not indicated in the material and methods
We thank the reviewer for their valuable comments and suggestions regarding Figure 3. Below, we detail the modifications made:
- Figure 3A: To address whether the reduced CAMSAP2 Golgi localization phenotype can be rescued, we overexpressed MARK2 cDNA in MARK2 KO cells. Our results show that overexpression of MARK2 successfully rescues the reduced CAMSAP2 localization to the Golgi, as demonstrated in Supplementary Figures 3C and 3E (page 8, lines 5-7).
- Figure 3F: We have removed the white dot on the HT1080 plot to ensure clarity and accuracy.
- Figure 3G: The composition of the homogenization buffer used in the experiment has been added to the Materials and Methods section for completeness (page 24, lines 34-41 and page 25, lines 1-10).
We hope these revisions address the reviewer’s concerns and enhance the clarity and rigor of our study. We are grateful for the reviewer’s constructive feedback, which has significantly improved the quality of our manuscript.
Figure 4
B: Quantification of the effect of the S835A mutation should be provided
D: Top left panel: Why Ha antibody stains Golgi structure in absence of Ha-CAMSAP2 transfection ? IF the Ha antibody has unspecific affinity towards the Golgi apparatus, may be it is not the good tag to use in this assay?
E: The number of cells studied should be standardized. 119 cells were analyzed in the CAMSAP KO vs only 35 cells in the CAMSAP2 KO (HA-CAMSAP2-S835D) conditions. This could introduce strong bias to the analysis. Furthermore the CAMSAP2 S835A seems to provide a certain level of rescue. It would be interesting to see what is the result of the T test between the HT1080 and HA-CAMSAP S835A conditions.
We thank the reviewer for their thoughtful comments and suggestions regarding Figure 4. Below, we detail the revisions and clarifications made:
- Figure 4B: The S835A mutation renders CAMSAP2 non-phosphorylatable by MARK2. This conclusion is based on our experimental observations and previously reported mechanisms.
- Figure 4D: The HA antibody does not exhibit non-specific affinity toward the Golgi apparatus. The observed labeling in the top left panel was due to an error in our annotation. We have corrected the label, replacing "HA" with "CAMSAP2" to accurately reflect the experimental conditions.
- Figure 4E: To standardize the number of cells analyzed across conditions, we reduced the number of CAMSAP2 KO cells analyzed to 50 and balanced the sample sizes for comparison. Additionally, we performed a t-test between the HT1080 and HACAMSAP2 S835A conditions. The results support that CAMSAP2 S835A provides partial rescue, as reflected in the updated analysis (page 32, lines 19-23).
We hope these revisions address the reviewer’s concerns and improve the accuracy and reliability of our results. We greatly appreciate the reviewer’s constructive feedback, which has significantly enhanced the quality of our study.
Figure 6
6A: The wound position should be indicated on the picture.
6B: Given that microtubule labelling is present on the vast majority of the cell surface, this type of quantification provides very little information using conventional light microscopy and should not be used to conclude any change in the microtubule network using Pearson's coefficient. The text describing the figure 6A and 6B needs re written as I do not understand what the author want to say. "In cells located before the wound edge..." : I do not understand how a cell could be located before the wound edge. Which figure corresponds to the trailing edge of the wounding?
We thank the reviewer for their valuable comments on Figure 6A (revised Supplementary Figure 6E) and Figure 6B (revised Supplementary Figure 6F). Below, we detail the modifications made:
- Figure 6A (revised Supplementary Figure 6E), we have added arrows to indicate the wound position, providing clearer guidance for interpreting the image.
- Figure 6B (revised Supplementary Figure 6F), we revised our quantification method based on the approach used in literature (Wu et al., 2016). Specifically, we analyzed the relationship between microtubules and the Golgi apparatus in cells at the leading edge of the wound. The x-axis represents the distance from the Golgi center, while the y-axis shows the normalized radial fluorescence intensity of microtubules and the Golgi apparatus.
Additionally, we revised the accompanying text for clarity and accuracy. The original description:
“In cells located before the wound edge, the Golgi apparatus maintained a ribbon-like shape, with a higher density of microtubules. In contrast, at the trailing edge of the wounding, the Golgi apparatus appeared more as stacks around the nucleus, with fewer microtubules” was replaced with:
“Finally, to comprehensively understand the dynamics between non-centrosomal microtubules and the Golgi apparatus during Golgi reorientation, we conducted cell wound-healing experiments (Supplementary Figure 6 E-F). Our observations revealed notable changes in the Golgi apparatus and microtubule network distribution in relation to the wounding. These findings corroborate our earlier results and suggest a highly dynamic interaction between the Golgi apparatus and microtubules during Golgi reorientation” (Revised manuscript page 11 lines 3-10).
We hope these changes address the reviewer’s concerns and improve the clarity and robustness of our study. We greatly appreciate the reviewer’s constructive feedback, which has significantly enhanced the presentation and interpretation of our data. References:
Wu, J., de Heus, C., Liu, Q., Bouchet, B.P., Noordstra, I., Jiang, K., Hua, S., Martin, M., Yang, C., Grigoriev, I., et al. (2016). Molecular Pathway of Microtubule Organization at the Golgi Apparatus. Dev Cell 39 (1): 44-60.
Reviewer #3:
Summary
In this study, Xu et al. analyzed the wound healing process of HT1080 cells to elucidate the molecular mechanisms by which the Golgi apparatus exhibits transient dispersion before reorienting to the wound edge in the compact assembly structure. They focused on the role of the microtubule minus-end binding protein CAMSAP2, which mediates the linkage between microtubules and the Golgi membrane. At first, they noticed that CAMSAP2 transiently lost Golgi colocalization during the initial phase of the wound healing process. They further found that the cell polarity-regulating kinase MARK2 binds and phosphorylates S835 of CAMSAP2, thereby enhancing the interaction between CAMSAP2 and the Golgi protein Uso1. Together with the phenotypes of CAMSAP2, MARK2, and Uso1 KO cells, these authors argue that the MARK2dependent phosphorylation of CAMSAP2 plays an important role in the reassembly and reorientation of the Golgi apparatus after a transient dispersion observed during the wound healing process.
We sincerely thank the reviewer for their thoughtful summary of our study and constructive feedback. Your comments have been invaluable in refining our research and enhancing the clarity and impact of our manuscript.
Major comments
(1) The premise of this study was that during the wound healing process, the Golgi apparatus exhibits transient dispersion before reorientation to the front of the nucleus.
In the first place, this claim has not been well established in previous studies or this paper. Therefore, the authors should present a proof of this claim in a clearer manner.
To introduce this cellular event, the authors cite several papers in the introduction (page 4) and the results (page 6) sections. However, many papers cited are review articles, and some of them do not describe this change in the Golgi assembly structure before reorientation. Only two original articles discussed this phenomenon (Bisel et al. 2008 and Wu et al. 2016), and direct evidence was provided by only one paper (Wu et al. 2016) in which changes in the Golgi apparatus in wound-healing RPE1 cells were recorded by live imaging (Fig.7A in Wu et al. 2016).
Furthermore, it should be noted that this previous paper demonstrated that depletion of CAMSAP2 inhibits Golgi dispersion. Obviously, this conclusion is inconsistent with their statement to introduce this study (page4) that ‟This emphasizes CAMSAP2's role in sustaining Golgi integrity during critical cellular events like migration." In addition, it also contradicts the authors' model of the present paper (Fig. 6E), which argued that disruption of the Golgi association of CAMSAP2 facilitates the Golgi dispersion.
We sincerely thank the reviewer for their detailed comments and for providing us with the opportunity to clarify the premise and conclusions of our study. Below, we address the main concerns raised:
First, to provide direct evidence of Golgi apparatus changes during the wound-healing process, we conducted live-cell imaging experiments. Our observations, presented in revised Supplementary Figure 2A, clearly demonstrate that the Golgi apparatus exhibits a transient dispersion state before reorienting toward the leading edge of the nucleus during migration.
Regarding the interpretation of previous studies, we acknowledge the reviewer’s concerns about the citation of review articles. To address this, we have revisited the literature and clarified that the phenomenon of Golgi dispersion during reorientation has been directly demonstrated in Wu et al (Wu et al., 2016), where live imaging of wound-healing RPE1 cells showed this dynamic behavior. Furthermore, we note that in Wu et al paper explicitly demonstrates that CAMSAP2 depletion promotes Golgi dispersion, contrary to the reviewer’s interpretation that "depletion of CAMSAP2 inhibits Golgi dispersion."
Our model focuses on the role of CAMSAP2 in restoring the Golgi from a transiently dispersed structure back to an intact ribbon-like structure during reorientation. Specifically, we propose that during this process, the disruption of CAMSAP2’s association with the Golgi affects this restoration, rather than directly promoting Golgi dispersion as suggested by the reviewer. We believe this distinction aligns with our data and the existing literature.
To strengthen the background of our study, we have revised the introduction and results sections (page 6, lines 6-13 and page 7, lines 1-17) to minimize reliance on review articles and have provided more explicit citations to original research papers. We hope this addresses the reviewer’s concern about the sufficiency of the cited literature.
We trust these clarifications and revisions resolve the reviewer’s concerns and enhance the robustness of our study. Once again, we are grateful for the reviewer’s constructive feedback, which has greatly helped refine our manuscript. References:
Wu, J., de Heus, C., Liu, Q., Bouchet, B.P., Noordstra, I., Jiang, K., Hua, S., Martin, M., Yang, C., Grigoriev, I., et al. (2016). Molecular Pathway of Microtubule Organization at the Golgi Apparatus. Dev Cell 39 (1): 44-60.
The authors did not provide experimental data for this temporal change in the Golgi assembly structures during the wound-healing process of HT1080 that they analyzed. They only provide an illustration of wound-healing cells (Fig.1F), in which cells are qualitatively discriminated and colored based on the Golgi states, without indicating the experimental basis of the discrimination.
According to their ambiguous descriptions in the text (page7), the reader can speculate that Fig. 1F is illustrated based on the images in Supplementary Fig. 2C. However, because of the low quality and presentation style of these data, it is impossible to recognize the assembly structures of the Golgi apparatus in wound-edge cells.
If the authors hope to establish this premise claim for the present paper, they should provide their own data corresponding to the present Supplementary Fig. 2C in more clarity and present qualitative data verifying this claim, as Wu et al. did in Fig. 7A in their paper.
We sincerely thank the reviewer for their constructive feedback and the opportunity to address the concern regarding the lack of experimental data supporting the temporal changes in Golgi assembly during the wound-healing process.
To establish this premise, we conducted live-cell imaging experiments to observe the dynamic changes in the Golgi apparatus during directed cell migration. Our data, now presented in Supplementary Figure 2A, clearly demonstrate that the Golgi apparatus undergoes a transient dispersed state before reorganizing into an intact structure. These findings provide direct experimental evidence supporting our claim.
In addition, we have revised the data originally presented in Supplementary Figure 2C and enhanced its quality and presentation style. This supplementary figure now includes clearer images and annotations to better illustrate the Golgi assembly structures in wound-edge cells. The improved data presentation aligns with the standards set by Wu et al reported (Wu et al., 2016) and provides qualitative support for our observations.
We hope these additions and revisions address the reviewer’s concerns and strengthen the scientific rigor and clarity of our manuscript. We are grateful for the reviewer’s valuable suggestions, which have significantly improved the quality of our study. References:
Wu, J., de Heus, C., Liu, Q., Bouchet, B.P., Noordstra, I., Jiang, K., Hua, S., Martin, M., Yang, C., Grigoriev, I., et al. (2016). Molecular Pathway of Microtubule Organization at the Golgi Apparatus. Dev Cell 39 (1): 44-60.
(2) In Fig.1A-D, the authors claim that CAMSAP2 dissociates from the Golgi apparatus in cells "that have not yet completed Golgi reorientation and exhibit a transitional Golgi structure, characterized by relative dispersion and loss of polarity (page7)." However, I these analyses, they do not analyze the initial stage (0.5h after wound addition) of cells facing the wound edge, as they do in Supplementary Fig. 2C. Instead, they analyze cells separated from the wound edge at 2 h after wound addition when the wound-edge cells complete their polarization. These data are highly misleading because there is no evidence that the cells separated from the wound edge are really in the transitional state before polarization.
In this regard, Fig. 1E shows the analysis of the wound-edge cells at 0.5 and 2 h after the addition of wound, which provides suitable data to verify the authors' claim. However, the corresponding legend indicates that these statistical data are based on the illustration in Fig. 1F, which is probably based on highly ambiguous data in Supplementary Fig. 2C (see above).
Taken together, I strongly recommend the authors to remove Fig.1A-D. Instead, they should include the improved figure corresponding to the present Supplementary Fig.2C and present its statistical analysis similar to the present Fig.1E for this claim.
We sincerely thank the reviewer for their constructive feedback and recommendations. Below, we address the concerns raised regarding Figure 1A-D and Supplementary Figure 2C.
To provide stronger evidence for the transitional state of the Golgi apparatus during reorientation and the dynamic regulation of CAMSAP2 localization, we conducted live-cell imaging experiments. These results, now presented in Supplementary Figure 2A, clearly demonstrate that the Golgi apparatus undergoes a transitional state characterized by dispersion before reorienting toward the leading edge.
Additionally, we analyzed fixed wound-edge cells at different time points during directed migration to observe CAMSAP2’s colocalization with the Golgi apparatus. The results, shown in Figures 1A and 1B, reveal dynamic changes in CAMSAP2 localization, confirm its regulation during Golgi reorientation, and include a corresponding statistical analysis (page 7, lines 1-17).
These updates ensure that our claims are supported by robust and unambiguous data.
We hope these revisions address the reviewer’s concerns and provide clear and reliable evidence for the transitional state of the Golgi apparatus and CAMSAP2’s dynamic regulation. We are grateful for the reviewer’s constructive suggestions, which have greatly improved the quality and focus of our manuscript.
(3) In Supplementary Fig. 5 and Fig. 4, the authors claim that MARK2 phosphorylates S835 of CAMSAP2.
There are many issues to be addressed. Otherwise, the above claim cannot be assumed to be reliable.
First, the descriptions (in the text and method sections) and figures (Supplementary Fig.5) concerning the in vitro kinase assay and subsequent phosphoproteomic analysis are too immature and contain many errors.
Legend to Supplementary Fig. 5 is too immature for comprehension. It should be completely rewritten in a more comprehensive manner. The figure in Supplementary Fig. 5C is also too immature for understanding. They simply paste raw mass spectrometric data without any modification for presentation.
We sincerely apologize for the lack of clarity and inaccuracies in the original descriptions and figure legends for the in vitro kinase assay and phosphoproteomic analysis. We greatly appreciate the reviewer’s detailed comments, which have allowed us to address these issues comprehensively.
To improve clarity and accuracy, we have rewritten the figure legend for the original Supplementary Figure 5 (now Supplementary Figure 4) as follows:
(A): CBB staining of a gel with GFP-CAMSAP2, GST, and GST-MARK2. GFP-CAMSAP2 was expressed in Sf9 cells and purified. GST and GST-MARK2 were expressed in E. coli and purified.
(B): Western blot analysis of an in vitro kinase assay. GST or GST-MARK2 was incubated with GFP-CAMSAP2 in kinase buffer (50 mM Tris-HCl pH 7.5, 12.5 mM MgCl2, 1 mM DTT, 400 μM ATP) at 30°C for 30 minutes. Reactions were stopped by boiling in the loading buffer.
(C): Detection of phosphorylation at S835 in CAMSAP2 by mass spectrometry. The observed mass increases in b4, b5, b6, b7, b8, b10, b11, and b12 fragments indicate phosphorylation at Ser835.
(D): Kinase assay samples analyzed using Phos-tag SDS-PAGE. HEK293 cells were cotransfected with the indicated plasmids. Band shifts of CAMSAP2 mutants were examined via western blot. Phos-tag was used in SDS-PAGE, and arrowheads indicate the shifted bands caused by phosphorylation.
To address the reviewer’s concern about Supplementary Figure 5C, we have reformatted the mass spectrometry data to improve readability and presentation quality. The revised figure includes clearer annotations and graphical representations of the mass spectrometric evidence for phosphorylation at S835.
We believe these updates enhance the comprehensibility and reliability of our data, providing robust support for our claim that MARK2 phosphorylates CAMSAP2 at S835. We hope these
revisions address the reviewer’s concerns and demonstrate our commitment to improving the quality of our manuscript.
The readers cannot understand how the authors purified GFP-CAMSAP2 for the kinase assay.
The method section incorrectly states that the product was purified using Ni-resin.
We thank the reviewer for their comment regarding the purification of GFP-CAMSAP2 for the kinase assay. We would like to clarify that GFP-CAMSAP2 carries a His-tag, which allows for purification using Ni-resin, as described in the Methods section (page 23, Lines 32-40). Therefore, the description in the Methods section is correct.
To avoid any potential misunderstanding, we have revised the Methods section to provide more detailed and precise descriptions of the purification process. Specifically, GFP-CAMSAP2 was cloned into the pOCC6_pOEM1-N-HIS6-EGFP vector, which includes a His-tag, and was expressed in Sf9 cells. The His-GFP-CAMSAP2 protein was purified using Ni-resin chromatography. Relevant details have been added to the Methods section (page 21, Lines 34-36:
“CAMSAP2 was cloned into the pOCC6_pOEM1-N-HIS6-EGFP vector expressed in Sf9, purified as His-GFP-CAMSAP2.”; page 23, Lines 32-33: “His-GFP-CAMSAP2 was cotransfected with bacmids into Sf9 cells to generate the passage 1 (P1) virus.”).
We hope these clarifications and revisions address the reviewer’s concern and improve the comprehensibility of our experimental details. We appreciate the reviewer’s feedback, which has helped us refine the manuscript.
In this relation, GST and GST-MARK2 are described as having been purified from Sf9 insect cells in the text section (page9) and legend to Supplementary Fig. 5, but from E. coli in the method section. Which is correct?
We thank the reviewer for pointing out the inconsistencies in the descriptions regarding the source of GST and GST-MARK2. To clarify, both GST and GST-MARK2 were purified from E. coli, as stated in the Methods section (page 23, Lines 26-31). We have corrected the erroneous descriptions in the main text (page 8, Lines 35-36) and the legend to Supplementary Figure 4 to ensure consistency.
Additionally, we have updated the legend for Supplementary Figure 4A to state the sources of each protein explicitly:
“GFP-CAMSAP2 were expressed in Sf9 cells and purified. GST and GST-MARK2 were expressed in E. coli and purified.” (page 38, Lines 2-3)
These revisions ensure that the experimental details are accurate and consistent across the manuscript, eliminating any potential confusion. We appreciate the reviewer’s careful review and constructive feedback, which have helped us improve the clarity and reliability of our study.
Because the phosphoproteomic data (Supplementary Fig. 5C) are not provided clearly, the experimental data for Fig.4A, in which possible CAMSAP2 phosphorylation sites are illustrated, are completely unknown. For me, it is highly strange that only the serine residues are listed in Fig. 4A.
We sincerely thank the reviewer for raising this important point regarding Figure 4A and the phosphoproteomic data in Supplementary Figure 5C.
- Phosphorylation Sites in Figure 4A
The phosphorylation sites illustrated in Figure 4A are derived from our analysis of the original mass spectrometry data. These sites were included based on their high confidence scores and data reliability. Importantly, only serine residues met the stringent criteria for inclusion, as no threonine or tyrosine residues had sufficient evidence for phosphorylation. To clarify this, we have updated the figure legend for Figure 4A (page 32, Lines3-7).
- Improvements to Supplementary Figure 5C (Supplementary Figure 4D in the revised manuscript)
To enhance transparency and clarity, we have reformatted Supplementary Figure 4D to include clearer annotations. The revised figure highlights the phosphopeptides used to identify the phosphorylation sites and provides a more comprehensive presentation of the mass spectrometry data. To clarify this, we have updated the figure legend for Supplementary Figure 4D (page 38, Lines 11-13).
- Data Availability
We will follow the journal’s guidelines by uploading the raw mass spectrometry data to the required public database upon manuscript acceptance. This ensures that the data are accessible and reproducible in compliance with journal standards.
We hope these clarifications and updates address the reviewer’s concerns and improve the reliability and comprehensibility of our data presentation. We greatly appreciate the reviewer’s constructive feedback, which has helped us enhance the rigor and clarity of our manuscript.
Considering the crude nature of the GST-MARK2 sample used for the in vitro kinase assay (Supplementary Fig. 5A), it is unclear whether MARK2 is responsible for all phosphorylation sites on CAMSAP2 detected in the phosphoproteomic analysis. Furthermore, if GFP-CAMSAP2 was purified from Sf9 insect cells, these sites might have been phosphorylated before incubation for the in vitro kinase assay. The authors should address these issues by including a negative control using the kinase-dead mutant of MARK2 in their in vitro kinase assay.
We sincerely thank the reviewer for raising these important points regarding the potential prephosphorylation of GFP-CAMSAP2 and the role of MARK2 in the phosphorylation sites detected in our analysis.
To address the possibility that GFP-CAMSAP2 may have been pre-phosphorylated during its expression in Sf9 insect cells, we conducted an in vitro comparison. Specifically, we compared the band shifts observed in GST-MARK2 + GFP-CAMSAP2 versus GST + GFP-CAMSAP2 under identical conditions. As shown in Supplementary Figure 4B, the GST-MARK2 + GFP-CAMSAP2 group exhibited a clear upward band shift compared to the GST + GFP-CAMSAP2 group, indicating additional phosphorylation events induced by MARK2.
Regarding the inclusion of a kinase-dead MARK2 mutant as a negative control, we acknowledge this as a valuable suggestion for further confirming the specificity of MARK2 in phosphorylating CAMSAP2. While this experiment is not currently included, we plan to conduct it in our future studies to strengthen our findings.
We hope this clarification and the provided evidence address the reviewer’s concerns. We are grateful for this constructive feedback, which has helped us critically evaluate and refine our experimental approach.
(4) In Supplementary Fig.6A-C and Fig.5A-B, the authors claim that the phosphorylation of CAMSAP2 S835 is required for restoring the reduced reorientation of the Golgi in wound-healing cells and the delay in wound closure observed in MARK2 KO cells.
If the aforementioned claim is adequately supported by experimental data, it indicates that the defects in Golgi repolarization and wound closure in MARK2 KO cells can be mainly attributed to the reduced phosphorylation of S835 of CAMSAP2 in HT1080. Considering the presence of many well-known substrates of MARK2 for regulating cell polarity, this claim is highly striking.
However, to strongly support this conclusion, the authors should first perform a rescue experiment using MARK2 KO cells exogenously expressing MARK2. This step is essential for determining whether the defects observed in MARK2 KO cells are caused by the loss of MARK2 expression, but not by other artificial effects that were accidentally raised during the generation of the present MARK2 KO clone.
We sincerely thank the reviewer for their insightful suggestion regarding the rescue experiment to confirm that the defects observed in MARK2 KO cells are specifically caused by the loss of MARK2 expression.
To address this, we performed a rescue experiment in MARK2 KO HT1080 cells by exogenously expressing GFP-MARK2. Our results, presented in Supplementary Figures 3C-E, demonstrate that GFP-MARK2 expression successfully restores the localization of CAMSAP2 on the Golgi apparatus in MARK2 KO cells.
These findings strongly support the conclusion that the defects in Golgi architecture and CAMSAP2 Golgi localization are directly attributable to the loss of MARK2 expression, rather than any artificial effects potentially introduced during the generation of the MARK2 KO clone.
We hope these additional experimental results address the reviewer’s concerns and provide robust evidence for the role of MARK2 in regulating Golgi reorientation and wound closure. We are grateful for the reviewer’s constructive feedback, which has significantly improved the rigor and clarity of our study.
In addition, to evaluate the impact of the rescue effect of CAMSAP2, the authors should include the data of wild-type HT1080 and MARK2 KO cells in Fig. 5B to reliably demonstrate the aforementioned claim.
We thank the reviewer for their valuable suggestion to include data from wild-type HT1080 and MARK2 KO cells in Figure 5A-C to better evaluate the rescue effects of CAMSAP2.
In response, we have incorporated data from wild-type HT1080 and MARK2 KO cells into Figure 5A-C. These additions provide a comprehensive comparison and further demonstrate the impact of CAMSAP2-S835A and CAMSAP2-S835D on Golgi reorientation relative to the wild-type and MARK2 KO conditions.
These changes are reflected in Figures 5A-C.
We hope these updates address the reviewer’s concerns and strengthen the reliability of our conclusions. We greatly appreciate the reviewer’s constructive feedback, which has significantly enhanced the robustness of our study.
Principally, before checking the rescue effects in MARK2 KO cells, the authors should examine the rescue activity of the CAMSAP2 S835 mutants in restoring the reduced reorientation of the Golgi in wound-healing cells and the delay in wound closure observed in CAMSAP2 KO cells (Supplementary Fig.1F-H and Supplementary Fig.2A, B). These experiments are more essential experiments to substantiate the authors' claim.
We thank the reviewer for their insightful suggestion to examine the rescue activity of CAMSAP2 S835 mutants in CAMSAP2 KO cells to further substantiate our claims.
In Figure 4D-F, we observed significant differences between CAMSAP2 S835 mutants in their ability to restore Golgi structure and localization, indicating functional differences between these mutants. To better reflect the regulatory role of MARK2-mediated phosphorylation of CAMSAP2, we performed scratch wound-healing experiments in MARK2 KO cells by establishing stable cell lines expressing CAMSAP2 S835 mutants. These experiments allowed us to assess Golgi reorientation during wound healing and are presented in Figure 5A-C.
We also attempted to generate stable cell lines expressing GFP-CAMSAP2 and its mutants in CAMSAP2 KO cells. Unfortunately, these cells consistently failed to survive, preventing successful construction of the cell lines.
We hope these experiments and explanations address the reviewer’s concerns. We are grateful for the reviewer’s constructive feedback, which has helped us refine and improve our study.
(5) The data presented in Fig. 6A and B are not sufficient to support the authors' notion that "our observation revealed notable changes in the Golgi apparatus and microtubule network distribution in relation to the wounding. (page 11)"
Fig. 6A, which includes only a single-cell image in each panel, does not demonstrate the general state of microtubules and the Golgi in the wound-edge cells. The reader cannot even know the migration direction of each cell.
Fig.6 B are not suitable to quantitatively support the authors' claim. The authors should find a way to quantitatively estimate the microtubule density around the Golgi and the shape and compactness of the Golgi in each cell facing the wound, not estimating the colocalization of microtubules and the Golgi, as in the present Fig. 6B.
We sincerely apologize for the confusion caused by our unclear descriptions and presentation.
Here, we clarify the purpose and improvements made to address the reviewer’s concerns. In this study, we primarily aimed to observe the relationship between microtubules and the Golgi apparatus in cells at the leading edge of the wound during directed migration. In Figure 6A (now Supplementary Figure 6E), the images represent cells located at the wound edge at different time points. To improve clarity, we have added arrows indicating the migration direction and updated the figure legend to describe these details (page 40 lines 13-14).
To better quantify the relationship between microtubules and the Golgi apparatus, we revised our analysis by referring to the quantitative method used in Figure 3F of the paper Molecular Pathway of Microtubule Organization at the Golgi Apparatus. Specifically, we performed a radial analysis of fluorescence intensity in cells at the wound edge, measuring the distance from the Golgi center (x-axis) and the normalized radial fluorescence intensity of microtubules and the Golgi (y-axis). These results are now presented in Supplementary Figure 6E and 6F.
We hope these improvements address the reviewer’s concerns and provide stronger evidence for the changes in the Golgi apparatus and microtubule network distribution in relation to wound healing. We greatly appreciate the reviewer’s constructive feedback, which has significantly enhanced the clarity and rigor of our study.
The legends to Fig. 6A and B indicate that they compared immunofluorescent staining of cells at the edge of the wound after 0.5h and 2 h of migration. However, the authors state in the text that they compared "the cells located before the wound" and "the cells at the trailing edge of the wounding (page 11)."Although this description is highly ambiguous and misleading, if they compared the wound-edge cells and the cells separated from the wound edge at 2 h after cell migration here, they should improve the experimental design as I pointed out in the 2nd major comment.
We thank the reviewer for their detailed feedback regarding the experimental design and the need to clarify our descriptions. We have addressed these concerns as follows:
- Clarification of descriptions:
We recognize that the previous description in the text regarding "the cells located before the wound" and "the cells at the trailing edge of the wounding" was ambiguous and potentially misleading. We have revised this text to accurately describe the experimental design. Specifically, we compared cells at the leading edge of the wound at different time points (0.5h and 2h post-migration). These corrections are reflected in figure legends (Supplementary Figure 6E and 6F ) and the Results section (page 11,lines 3-8).
- Improved experimental design:
To better support our conclusions, we performed live-cell imaging to observe the dynamic changes in the Golgi apparatus during directed migration. As shown in Supplementary Figure 2A, our results confirm that the Golgi apparatus undergoes a transient dispersed state before reorganizing into an intact structure.
Additionally, we performed fixed-cell staining at different time points to analyze the colocalization of CAMSAP2 with the Golgi apparatus in cells at the leading edge of the wound. The colocalization analysis, presented in Figures 1A-C, further demonstrates the dynamic regulation of CAMSAP2 during Golgi reorientation.
We hope these updates address the reviewer’s concerns and provide a clearer and more robust foundation for our conclusions. We are grateful for the reviewer’s constructive feedback, which has greatly enhanced the clarity and rigor of our study.
Minor comments
(1) In Fig. 2 and Supplementary Fig. 3, the authors claim that MARK2 is enriched around the Golgi. However, this claim was based on immunofluorescent images of single cells and single-line scans.
It is better to present the statistical data for Pearson's coefficient as shown in Figs. 1D and E. To demonstrateMARK2 enrichment around Golgi, but not localization in Golgi, the authors should find a way to quantify the specific enrichment of MARK2 signals in the Golgi region.
We thank the reviewer for raising this important point regarding the enrichment of MARK2 around the Golgi apparatus. Upon further consideration, we acknowledge that our current data do not provide sufficient evidence to fully elucidate the mechanism of MARK2 localization to the Golgi.
To maintain the scientific rigor of our study, we have removed this claim and the corresponding content from the manuscript, including original Figures 2 and Supplementary Figure 3 that specifically discuss MARK2 enrichment. These changes do not affect the primary conclusions of the study, which focus on the role of MARK2-mediated phosphorylation of CAMSAP2.
We hope this clarification addresses the reviewer’s concerns. In the future, we plan to investigate the precise mechanism of MARK2 localization using additional experimental approaches. We are grateful for the reviewer’s constructive feedback, which has helped us refine the scope and focus of our manuscript.
(2) In Fig. 3 and Supplementary Fig. 4, the authors report that CAMSAP2 localization on the Golgi is reduced in cells lacking MARK2.
Essentially, the present results support this claim. However, the authors should analyze the Golgi localization of CAMASP2 with the same quantification parameter because they used Pearson's coefficient in Fig. 1D, E and Supplementary Fig.4D but Mander's coefficient in Fig. 3C and Fig.4F.
We thank the reviewer for their insightful comment regarding the consistency of quantification parameters used in our analysis of CAMSAP2 localization on the Golgi apparatus.
To address this concern, we have revised Figure 3C to use Pearson’s coefficient for consistency with Figure 1D, 1E (Figure 1B and 1E in the revised manuscript), and Supplementary Figure 4D (Supplementary Figure 3I in the revised manuscript). This ensures uniformity in the quantification parameters across these analyses.
For Figure 4F, we have retained Mander’s coefficient, as it accounts for variability in expression levels due to overexpression in individual cells. We believe this approach provides a more accurate reflection of CAMSAP2 localization under the experimental conditions shown in Figure 4F.
We hope these adjustments clarify our analysis and address the reviewer’s concerns. We greatly appreciate the reviewer’s constructive feedback, which has helped improve the consistency and accuracy of our study.
(3) In Fig.4D-F, the authors claim that S835 phosphorylation of CAMSAP2 is essential for its localization to the Golgi apparatus and for restoring the Golgi dispersion induced by CAMASAP2 depletion.
Fig.4E indicates that the S835A mutant of CAMSAP2 significantly restores the compact assembly of the Golgi apparatus, and the differences in the rescue activities of the wild type, S835A, and S835D are rather small. These data contradict the authors' conclusions regarding the pivotal role of MARK2-mediated phosphorylation at the S835 site of CAMSAP2 in maintaining the Golgi architecture (page 9). The authors should remove the phrase "MARK2-mediated" from the sentence unless addressing the aforementioned issues (see 3rd major comment) and describe the role of S835 phosphorylation in more subdued tone.
We thank the reviewer for their constructive feedback regarding the conclusions drawn about the role of MARK2-mediated phosphorylation of CAMSAP2 at S835.
In response, we have revised the relevant sentence to reflect a more nuanced interpretation of the data. Specifically, the original statement:
“These observations indicate that the phosphorylation of serine 835 in CAMSAP2 is essential for its proper localization to the Golgi apparatus.”
has been updated to:
“These observations indicate that MARK2 phosphorylation of serine at position 835 of CAMSAP2 affects the localization of CAMSAP2 on the Golgi and regulates Golgi structure” (page 9, Lines 27-29).
We hope this modification addresses the reviewer’s concerns. We are grateful for the feedback, which has helped us refine our conclusions and enhance the clarity of our manuscript.
(4) In Figs. 5I, J and Supplementary Fig.7A-E, the authors claim that the S835 phosphorylationdependent interaction of CAMSAP2 with Uso1 is essential for its localization to the Golgi apparatus.
This claim was made based on immunofluorescent images of single cells and single-line scans, and was not sufficiently verified (Supplementary Fig.7B, C). Because this is a crucial claim for the present paper, the authors should present statistical data for Pearson's coefficient, as shown in Fig. 1D and E, to quantitatively estimate the Golgi localization of CAMSAP2.
We thank the reviewer for their suggestion to present statistical data using Pearson's coefficient for a more robust quantification of the Golgi localization of CAMSAP2.
In response, we have revised the statistical analysis for Supplementary Figures 7B-C (Revised Figures 6F and 6G) to use Pearson's coefficient. This change ensures consistency with the quantification methods used in Figures 1D and 1E (Revised Figures 1B and 1E), allowing for a more standardized evaluation of CAMSAP2’s localization to the Golgi apparatus.
We hope this modification addresses the reviewer’s concerns and strengthens the quantitative support for our claims. We are grateful for the reviewer’s constructive feedback, which has helped improve the rigor of our study.
(5) The signal intensities of the immunofluorescent data in Fig. 4D, Fig. 5A, Sup-Fig. 3C and E, and Sup-Fig. 7S are very weak for readers to clearly estimate the authors' claims. They should be improved appropriately.
We thank the reviewer for highlighting the need to improve the clarity of the immunofluorescent data presented in several figures.
In response, we have enhanced the signal intensities in Figures 4D, 5A, and Supplementary Figure 7D (Revised Supplementary Figure 6A) to make the signals clearer for readers, while ensuring that the adjustments do not alter the integrity of the original data. Supplementary Figures 3C and 3E was remove from our manuscript.
Additionally, to improve consistency and readability across the manuscript, we have standardized the quantification methods for similar analyses:
For CAMSAP2 localization to the Golgi, Pearson's coefficient has been used throughout the manuscript. Figure 3C has been updated to use Pearson's coefficient for consistency.
For Golgi state analysis in wound-edge cells, we have used the Golgi position relative to the nucleus as a uniform metric. This has been applied to Supplementary Figures 1F and 1G, Figures 2D and 2E, and Figures 5A and 5B.
We hope these adjustments address the reviewer’s concerns and improve the clarity and consistency of our study. We greatly appreciate the reviewer’s constructive feedback, which has significantly enhanced the quality of our manuscript.
(6) As indicated above, the authors frequently change the parameters or methods for quantifying the same phenomena (for example, the localization of CAMSAP on the Golgi and Golgi state in wound edge cells) in each figure. This is highly confusing. They should unify them.
We thank the reviewer for their valuable feedback regarding the inconsistency in quantification methods across the manuscript.
To address this concern, we have carefully reviewed the entire manuscript and standardized the methods used for quantifying similar phenomena:
- CAMSAP2 localization on the Golgi:
Pearson's coefficient is now consistently used throughout the manuscript. For example, Figure 3C has been updated to use Pearson's coefficient to align with other figures, such as Figures 1B and 1E.
- Golgi state in wound-edge cells:
The Golgi state is now uniformly measured based on the position of the Golgi relative to the nucleus. This method has been applied to Supplementary Figures 1F and 1G, Figures 2D and 2E, and Figures 5A and 5B.
We believe these changes significantly improve the clarity and consistency of the manuscript, ensuring that readers can easily interpret the data. We are grateful for the reviewer’s constructive feedback, which has greatly helped us enhance the quality and rigor of our study.
(7) The legends frequently fail to clearly indicate the number of independent experiments on which each statistical analysis was based.
We thank the reviewer for highlighting the need to clearly indicate the number of independent experiments for each statistical analysis.
In response, we have carefully reviewed the entire manuscript and updated the figure legends to include the number of independent experiments for every statistical analysis. This ensures transparency and allows readers to better evaluate the reliability of the data.
We hope these updates address the reviewer’s concerns and improve the clarity and rigor of the manuscript. We appreciate the reviewer’s constructive feedback, which has helped us enhance the quality of our work.
(8) Supplemental Figs. 4E and 4F are not cited in the text.
We thank the reviewer for pointing out that Supplemental Figures 4E and 4F were not cited in the text.
To address this, we have updated the manuscript to cite these figures (Revised Figures 2H and 2I) in the appropriate section (page 8, lines 1-5).
“the absence of MARK2 can also influence the orientation of the Golgi apparatus during cell wound healing and cause a delay in wound closure (Figure 2 D-I and Figure 3 D).”
We hope this revision resolves the reviewer’s concern and improves the clarity and completeness of the manuscript. We appreciate the reviewer’s feedback, which has helped us refine our work.
(9) The data in Fig. 3 analyzed MARK2 knockout cells (not knockdown cells). The caption should be corrected.
We thank the reviewer for pointing out the incorrect use of "knockdown" in the caption of Figure 3.
To address this, we have revised the title of Figure 3 from:
“MARK2 knockdown reduces CAMSAP2 localization on the Golgi apparatus.”
to:
“MARK2 affects CAMSAP2 localization on the Golgi apparatus.”
This updated caption reflects the inclusion of both MARK2 knockout and knockdown cell lines analyzed in Figure 3.
We hope this correction resolves the reviewer’s concern and ensures the accuracy of our manuscript. We greatly appreciate the reviewer’s attention to detail, which has helped us improve the clarity and consistency of our work.
(10) The present caption in Fig. 6 disagrees with the content of the figure.
We thank the reviewer for pointing out the inconsistency between the caption and the content of Figure 6.
To address this issue, we have revised the content of Figure 6 to ensure it aligns accurately with the caption. The updated figure now reflects the description provided in the caption, eliminating any discrepancies and improving clarity for the readers.
We appreciate the reviewer’s constructive feedback, which has helped us enhance the accuracy and presentation of our manuscript.
(11) What do "CS" indicate in Fig. 4B and Supplementary Fig. 5D? The style used to indicate point mutants of CAMSAP2 should be unified. 835A or S835A?
We thank the reviewer for pointing out the inconsistency in the naming of CAMSAP2 mutants.
To address this, we have revised all relevant figures and text to use the consistent format "S835A" and "S589A" for CAMSAP2 mutants. Specifically, in Figure 4B and Supplementary Figure 5D (now Supplementary Figure 4C), we have replaced the abbreviation "CS2" with "CAMSAP2" and updated the mutant names from "835A" and "589A" to "S835A" and "S589A," respectively. We hope these updates resolve the reviewer’s concerns and ensure clarity and consistency throughout the manuscript. We are grateful for the reviewer’s attention to detail, which has helped us improve the quality of our work.
(12) Uso1 is not a Golgi matrix protein.
We thank the reviewer for pointing out the incorrect description of Uso1 as a Golgi matrix protein.
In response, we have revised the manuscript to replace all references to “USO1 as a Golgi matrix protein” with “USO1 as a Golgi-associated protein.” This correction ensures that the terminology used in the manuscript is accurate and consistent with current scientific understanding.
We appreciate the reviewer’s attention to detail, which has helped us improve the accuracy and quality of our manuscript.
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www.reddit.com www.reddit.com
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There's a few things going on here. Generally at SGW a gray Olympia SM3 in excellent "looking" condition like this one will go for $120-150. This one is also hiding a script typeface which will usually add another $110-150 of value, which would put it at the $300 mark. I'm sort of surprised that the original winner didn't actually pay for it at this price as that's likely what someone would honestly pay for one like this. (It's also possible that they forgot they won or didn't know and didn't pay for it in time too.)
On today's listing, it's far, far more likely that someone wants it and either couldn't get it or pay for it now at the price that it was going to go for in a reasonable auction. They used a throw away accout to make an outrageous bid in hopes that in a week it'll be relisted and no one will notice the script typeface and it'll go for well under $200. (It won't.) This happens incredibly frequently for some of the less common typewriters. Usually it's machines with script or uncommon typefaces or uncommon character sets. Recent auctions for a gold plated Olympia SM3 and a Yellow Royal FP with a Gothic typeface come to mind. I've seen this also happen four or five times in a row before someone ultimately pays for a machine at some reasonable price.
Honestly, SGW should have a policy that the second and third runners up for auctions that don't get paid for by winners should have the right of last refusal on auctions like this to prevent this sort of "gaming" of the system. If you search back in this sub, you'll see this topic coming up every couple of weeks with the same discussions over and over. The common wisdom is that a SGW auction isn't gone until the machine doesn't pop up anymore and actually "sold". And even then, if you wait a week or two, you'll usually see the exact machine pop up less than a month later on eBay being listed by the winner for an exorbitant amount (almost always without having done any additional cleaning or restoration work on it aside from maybe dusting it out.)
Maybe we should add the tag #SGWgaming to all these conversations to make them easier to find?
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docdrop.org docdrop.org
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Numbers are not neutral
should be the tag line of our class haha
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cheatsheetseries.owasp.org cheatsheetseries.owasp.org
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Once an authenticated session has been established, the session ID (or token) is temporarily equivalent to the strongest authentication method used by the application, such as username and password, passphrases, one-time passwords (OTP),
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www.wboy.com www.wboy.com
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McCuskey said that while many fans see the tournament as a fun way to fill out a bracket, the tournament is, in fact, a multi-billion-dollar business, as well as the pinnacle of many student-athletes’ college careers. try { var event = new CustomEvent("nsDfpSlotRendered", { detail: { id: "acm-ad-tag-mr2_ab-mr2_ab" } }); console.log("HTL.nsDfpSlotRendered", event); window.dispatchEvent(event); } catch (err) {}
Leaving WVU didn't only affect the fans and the players it also affected the entire state of West Virginia's potential economy growth
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www.biorxiv.org www.biorxiv.org
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Reviewer #1 (Public review):
Summary:
This study aims to provide imaging methods for users of the field of human layer-fMRI. This is an emerging field with 240 papers published so far. Different than implied in the manuscript, 3T is well represented among those papers. E.g. see the papers below that are not cited in the manuscript. Thus, the claim on the impact of developing 3T methodology for wider dissemination is not justified. Specifically, because some of the previous papers perform whole brain layer-fMRI (also at 3T) in more efficient, and more established procedures.
The authors implemented a sequence with lots of nice features. Including their own SMS EPI, diffusion bipolar pulses, eye-saturation bands, and they built their own reconstruction around it. This is not trivial. Only a few labs around the world have this level of engineering expertise. I applaud this technical achievement. However, I doubt that any of this is the right tool for layer-fMRI, nor does it represent an advancement for the field. In the thermal noise dominated regime of sub-millimeter fMRI (especially at 3T) it is established to use 3D readouts over 2D (SMS) readouts. While it is not trivial to implement SMS, the vendor implementations (as well as the CMRR and MGH implementations) are most widely applied across the majority of current fMRI studies already. The author's work on this does not serve any previous shortcomings in the field.
The mechanism to use bi-polar gradients to increase the localization specificity is doubtful to me. In my understanding, killing the intra-vascular BOLD should make it less specific. Also, the empirical data do not suggest a higher localization specificity to me.
Embedding this work in the literature of previous methods is incomplete. Recent trends of vessel signal manipulation with ABC or VAPER are not mentioned. Comparisons with VASO are outdated and incorrect.
The reproducibility of the methods and the result is doubtful (see below).
I don't think that this manuscript is in the top 50% of the 240 layer-fmri papers out there.
3T layer-fMRI papers that are not cited:
Taso, M., Munsch, F., Zhao, L., Alsop, D.C., 2021. Regional and depth-dependence of cortical blood-flow assessed with high-resolution Arterial Spin Labeling (ASL). Journal of Cerebral Blood Flow and Metabolism. https://doi.org/10.1177/0271678X20982382
Wu, P.Y., Chu, Y.H., Lin, J.F.L., Kuo, W.J., Lin, F.H., 2018. Feature-dependent intrinsic functional connectivity across cortical depths in the human auditory cortex. Scientific Reports 8, 1-14. https://doi.org/10.1038/s41598-018-31292-x
Lifshits, S., Tomer, O., Shamir, I., Barazany, D., Tsarfaty, G., Rosset, S., Assaf, Y., 2018. Resolution considerations in imaging of the cortical layers. NeuroImage 164, 112-120. https://doi.org/10.1016/j.neuroimage.2017.02.086
Puckett, A.M., Aquino, K.M., Robinson, P.A., Breakspear, M., Schira, M.M., 2016. The spatiotemporal hemodynamic response function for depth-dependent functional imaging of human cortex. NeuroImage 139, 240-248. https://doi.org/10.1016/j.neuroimage.2016.06.019
Olman, C.A., Inati, S., Heeger, D.J., 2007. The effect of large veins on spatial localization with GE BOLD at 3 T: Displacement, not blurring. NeuroImage 34, 1126-1135. https://doi.org/10.1016/j.neuroimage.2006.08.045
Ress, D., Glover, G.H., Liu, J., Wandell, B., 2007. Laminar profiles of functional activity in the human brain. NeuroImage 34, 74-84. https://doi.org/10.1016/j.neuroimage.2006.08.020
Huber, L., Kronbichler, L., Stirnberg, R., Ehses, P., Stocker, T., Fernández-Cabello, S., Poser, B.A., Kronbichler, M., 2023. Evaluating the capabilities and challenges of layer-fMRI VASO at 3T. Aperture Neuro 3. https://doi.org/10.52294/001c.85117
Scheeringa, R., Bonnefond, M., van Mourik, T., Jensen, O., Norris, D.G., Koopmans, P.J., 2022. Relating neural oscillations to laminar fMRI connectivity in visual cortex. Cerebral Cortex. https://doi.org/10.1093/cercor/bhac154
Strengths:
See above. The authors developed their own SMS sequence with many features. This is important to the field. And does not leave sequence development work to view isolated monopoly labs. This work democratises SMS.<br /> The questions addressed here are of high relevance to the field: getting tools with good sensitivity, user-friendly applicability, and locally specific brain activity mapping is an important topic in the field of layer-fMRI.
Weaknesses:
(1) I feel the authors need to justify why flow-crushing helps localization specificity. There is an entire family of recent papers that aims to achieve higher localization specificity by doing the exact opposite. Namely, MT or ABC fRMRI aims to increase the localization specificity by highlighting the intravascular BOLD by means of suppressing non-flowing tissue. To name a few:
Priovoulos, N., de Oliveira, I.A.F., Poser, B.A., Norris, D.G., van der Zwaag, W., 2023. Combining arterial blood contrast with BOLD increases fMRI intracortical contrast. Human Brain Mapping hbm.26227. https://doi.org/10.1002/hbm.26227.
Pfaffenrot, V., Koopmans, P.J., 2022. Magnetization Transfer weighted laminar fMRI with multi-echo FLASH. NeuroImage 119725. https://doi.org/10.1016/j.neuroimage.2022.119725
Schulz, J., Fazal, Z., Metere, R., Marques, J.P., Norris, D.G., 2020. Arterial blood contrast ( ABC ) enabled by magnetization transfer ( MT ): a novel MRI technique for enhancing the measurement of brain activation changes. bioRxiv. https://doi.org/10.1101/2020.05.20.106666
Based on this literature, it seems that the proposed method will make the vein problem worse, not better. The authors could make it clearer how they reason that making GE-BOLD signals more extra-vascular weighted should help to reduce large vein effects.
The empirical evidence for the claim that flow crushing helps with the localization specificity should be made clearer. The response magnitude with and without flow crushing looks pretty much identical to me (see Fig, 6d).<br /> It's unclear to me what to look for in Fig. 5. I cannot discern any layer patterns in these maps. It's too noisy. The two maps of TE=43ms look like identical copies from each other. Maybe an editorial error?
The authors discuss bipolar crushing with respect to SE-BOLD where it has been previously applied. For SE-BOLD at UHF, a substantial portion of the vein signal comes from the intravascular compartment. So I agree that for SE-BOLD, it makes sense to crush the intravascular signal. For GE-BOLD however, this reasoning does not hold. For GE-BOLD (even at 3T), most of the vein signal comes from extravascular dephasing around large unspecific veins and the bipolar crushing is not expected to help with this.
(2) The bipolar crushing is limited to one single direction of flow. This introduces a lot of artificial variance across the cortical folding pattern. This is not mentioned in the manuscript. There is an entire family of papers that perform layer-fmri with black-blood imaging that solves this with a 3D contrast preparation (VAPER) that is applied across a longer time period, thus killing the blood signal while it flows across all directions of the vascular tree. Here, the signal cruising is happening with a 2D readout as a "snap-shot" crushing. This does not allow the blood to flow in multiple directions.<br /> VAPER also accounts for BOLD contaminations of larger draining veins by means of a tag-control sampling. The proposed approach here does not account for this contamination.
Chai, Y., Li, L., Huber, L., Poser, B.A., Bandettini, P.A., 2020. Integrated VASO and perfusion contrast: A new tool for laminar functional MRI. NeuroImage 207, 116358. https://doi.org/10.1016/j.neuroimage.2019.116358
Chai, Y., Liu, T.T., Marrett, S., Li, L., Khojandi, A., Handwerker, D.A., Alink, A., Muckli, L., Bandettini, P.A., 2021. Topographical and laminar distribution of audiovisual processing within human planum temporale. Progress in Neurobiology 102121. https://doi.org/10.1016/j.pneurobio.2021.102121
If I would recommend anyone to perform layer-fMRI with blood crushing, it seems that VAPER is the superior approach. The authors could make it clearer why users might want to use the unidirectional crushing instead.
(3) The comparison with VASO is misleading.<br /> The authors claim that previous VASO approaches were limited by TRs of 8.2s. The authors might be advised to check the latest literature of the last years.<br /> Koiso et al. has performed whole brain layer-fMRI VASO at 0.8mm at 3.9 seconds (with reliable activation) and 2.7 seconds (with unconvincing activation pattern, though), and 2.3 (without activation).<br /> Also, whole brain layer-fMRI BOLD at 0.5mm and 0.7mm has been previously performed by the Juelich group at TRs of 3.5s (their TR definition is 'fishy' though).
Koiso, K., Müller, A.K., Akamatsu, K., Dresbach, S., Gulban, O.F., Goebel, R., Miyawaki, Y., Poser, B.A., Huber, L., 2023. Acquisition and processing methods of whole-brain layer-fMRI VASO and BOLD: The Kenshu dataset. Aperture Neuro 34. https://doi.org/10.1101/2022.08.19.504502
Yun, S.D., Pais‐Roldán, P., Palomero‐Gallagher, N., Shah, N.J., 2022. Mapping of whole‐cerebrum resting‐state networks using ultra‐high resolution acquisition protocols. Human Brain Mapping. https://doi.org/10.1002/hbm.25855
Pais-Roldan, P., Yun, S.D., Palomero-Gallagher, N., Shah, N.J., 2023. Cortical depth-dependent human fMRI of resting-state networks using EPIK. Front. Neurosci. 17, 1151544. https://doi.org/10.3389/fnins.2023.1151544
The authors are correct that VASO is not advised as a turn-key method for lower brain areas, incl. Hippocampus and subcortex. However, the authors use this word of caution that is intended for inexperienced "users" as a statement that this cannot be performed. This statement is taken out of context. This statement is not from the academic literature. It's advice for the 40+ user base that want to perform layer-fMRI as a plug-and-play routine tool in neuroscience usage. In fact, sub-millimeter VASO is routinely being performed by MRI-physicists across all brain areas (including deep brain structures, hippocampus etc). E.g. see Koiso et al. and an overview lecture from a layer-fMRI workshop that I had recently attended: https://youtu.be/kzh-nWXd54s?si=hoIJjLLIxFUJ4g20&t=2401
Thus, the authors could embed this phrasing into the context of their own method that they are proposing in the manuscript. E.g. the authors could state whether they think that their sequence has the potential to be disseminated across sites, considering that it requires slow offline reconstruction in Matlab?<br /> Do the authors think that the results shown in Fig. 6c are suggesting turn-key acquisition of a routine mapping tool? In my humble opinion it looks like random noise, with most of the activation outside the ROI (in white matter).
(4) The repeatability of the results is questionable.<br /> The authors perform experiments about the robustness of the method (line 620). The corresponding results are not suggesting any robustness to me. In fact the layer profiles in Fig. 4c vs. Fig 4d are completely opposite. Location of peaks turn into locations of dips and vice versa.<br /> The methods are not described in enough detail to reproduce these results.<br /> The authors mention that their image reconstruction is done "using in-house MATLAB code" (line 634). They do not post a link to github, nor do they say if they share this code.
It is not trivial to get good phase data for fMRI. The authors do not mention how they perform the respective coil-combination.<br /> No data are shared for reproduction of the analysis.
(5) The application of NODRIC is not validated.<br /> Previous applications of NORDIC at 3T layer-fMRI have resulted in mixed success. When not adjusted for the right SNR regime it can result in artifactual reductions of beta scores, depending on the SNR across layers. The authors could validate their application of NORDIC and confirm that the average layer-profiles are unaffected by the application of NORDIC. Also, the NORDIC version should be explicitly mentioned in the manuscript.
Akbari, A., Gati, J.S., Zeman, P., Liem, B., Menon, R.S., 2023. Layer Dependence of Monocular and Binocular Responses in Human Ocular Dominance Columns at 7T using VASO and BOLD (preprint). Neuroscience. https://doi.org/10.1101/2023.04.06.535924
Knudsen, L., Guo, F., Huang, J., Blicher, J.U., Lund, T.E., Zhou, Y., Zhang, P., Yang, Y., 2023. The laminar pattern of proprioceptive activation in human primary motor cortex. bioRxiv. https://doi.org/10.1101/2023.10.29.564658
Comments on revisions:
Among all the concerns mentioned above, I think there is only one of the specific issues that was sufficiently addressed.<br /> The authors implemented a combination of three consecutive-dimensional flow crushers. Other concerns were not sufficiently addressed to change my confidence level of the study.<br /> - While the abstract is still focusing on the utility of using 3T, they do not give credit to early 3T layer-fMRI papers leading the way to larger coverage and connectivity applications.<br /> - While the author's choice of using custom SMS 2D readout is justified for them. I do not think that this very method will utilize widespread 3T whole brain connectivity experiments across the global 3T community. This lowers the impact of the paper.<br /> - The images in Fig. 5 are still suspiciously similar. To the level that the noise pattern outside the brain is identical across large parts of the maps with and without PR.<br /> - Maybe it's my ignorance, but I still do not agree why flow crushing focuses the local BOLD responses to small vessels.<br /> - While my feel of a misleading representation of the literature had been accompanied by explicit references, the authors claim that they cannot find them?!? Or claim that they are about something else (which they are not, in my viewpoint).<br /> Data and software are still not shared (not even example data, or nii data).
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Author response:
The following is the authors’ response to the original reviews.
General responses:
The authors sincerely thank all the reviewers for their valuable and constructive comments. We also apologize for the long delay in providing this rebuttal due to logistical and funding challenges. In this revision, we modified the bipolar gradients from one single direction to all three directions. Additionally, in response to the concerns regarding data reliability, we conducted a thorough examination of each step in our data processing pipeline. In the original processing workflow, the projection-onto-convex-set (POCS) method was used for partial Fourier reconstruction. Upon examination, we found that applying the POCS method after parallel image reconstruction significantly altered the signal and resulted in considerable loss of functional feature. Futhermore, the original scan protocol employed a TE of 46 ms, which is notably longer than the typical TE of 33 ms. A prolonged TE can increase the ratio of extravascular to intravascular contributions. Importantly, the impact of TE on the efficacy of phase regression remains unclear, introducing potential confounding effects. To address these issues, we revised the protocol by shortening the TE from 46 ms to 39 ms. This adjustment was achieved by modifying the SMS factor to 3 and the in-plane acceleration rate to 3, thereby minimizing the confounding effects associated with an extended TE.
Following these changes, we recollected task-based fMRI data (N=4) and resting-state fMRI data (N=14) under the updated protocol. Using the revised dataset, we validated layer-specific functional connectivity (FC) through seed-based analyses. These analyses revealed distinct connectivity patterns in the superficial and deep layers of the primary motor cortex (M1), with statistically significant inter-layer differences. Furthermore, additional analyses with a seed in the primary sensory cortex (S1) corroborated the robustness and reliability of the revised methodology. We also changed the ‘directed’ functional connectivity in the title to ‘layer-specific’ functional connectivity, as drawing conclusions about directionality requires auxiliary evidence beyond the scope of this study.
We provide detailed responses to the reviewers’ comments below.
Reviewer #1 (Public Review):
Summary:
(1) This study aims to provide imaging methods for users of the field of human layer-fMRI. This is an emerging field with 240 papers published so far. Different than implied in the manuscript, 3T is well represented among those papers. E.g. see the papers below that are not cited in the manuscript. Thus, the claim on the impact of developing 3T methodology for wider dissemination is not justified. Specifically, because some of the previous papers perform whole brain layer-fMRI (also at 3T) in more efficient, and more established procedures.
3T layer-fMRI papers that are not cited:
Taso, M., Munsch, F., Zhao, L., Alsop, D.C., 2021. Regional and depth-dependence of cortical blood-flow assessed with high-resolution Arterial Spin Labeling (ASL). Journal of Cerebral Blood Flow and Metabolism. https://doi.org/10.1177/0271678X20982382
Wu, P.Y., Chu, Y.H., Lin, J.F.L., Kuo, W.J., Lin, F.H., 2018. Feature-dependent intrinsic functional connectivity across cortical depths in the human auditory cortex. Scientific Reports 8, 1-14. https://doi.org/10.1038/s41598-018-31292-x
Lifshits, S., Tomer, O., Shamir, I., Barazany, D., Tsarfaty, G., Rosset, S., Assaf, Y., 2018. Resolution considerations in imaging of the cortical layers. NeuroImage 164, 112-120. https://doi.org/10.1016/j.neuroimage.2017.02.086
Puckett, A.M., Aquino, K.M., Robinson, P.A., Breakspear, M., Schira, M.M., 2016. The spatiotemporal hemodynamic response function for depth-dependent functional imaging of human cortex. NeuroImage 139, 240-248. https://doi.org/10.1016/j.neuroimage.2016.06.019
Olman, C.A., Inati, S., Heeger, D.J., 2007. The effect of large veins on spatial localization with GE BOLD at 3 T: Displacement, not blurring. NeuroImage 34, 1126-1135. https://doi.org/10.1016/j.neuroimage.2006.08.045
Ress, D., Glover, G.H., Liu, J., Wandell, B., 2007. Laminar profiles of functional activity in the human brain. NeuroImage 34, 74-84. https://doi.org/10.1016/j.neuroimage.2006.08.020
Huber, L., Kronbichler, L., Stirnberg, R., Ehses, P., Stocker, T., Fernández-Cabello, S., Poser, B.A., Kronbichler, M., 2023. Evaluating the capabilities and challenges of layer-fMRI VASO at 3T. Aperture Neuro 3. https://doi.org/10.52294/001c.85117
Scheeringa, R., Bonnefond, M., van Mourik, T., Jensen, O., Norris, D.G., Koopmans, P.J., 2022. Relating neural oscillations to laminar fMRI connectivity in visual cortex. Cerebral Cortex. https://doi.org/10.1093/cercor/bhac154
We thank the reviewer for listing out 8 papers related to 3T layer-fMRI papers. The primary goal of our work is to develop a methodology for brain-wide, layer-dependent resting-state functional connectivity at 3T. Upon review of the cited papers, we found that:
(1) One study (Lifshits et al.) was not an fMRI study.
(2) One study (Olman et al.) was conducted at 7T, not 3T.
(3) Two studies (Taso et al. and Wu et al.) employed relatively large voxel sizes (1.6 × 2.3 × 5 mm³ and 1.5 mm isotropic, respectively), which limits layer specificity.
(4) Only one of the listed studies (Huber et al., Aperture Neuro 2023) provides coverage of more than half of the brain.
While each of these studies offers valuable insights, the VASO study by Huber et al. is the most relevant to our work, given its brain-wide coverage. However, the VASO method employs a relatively long TR (14.137 s), which may not be optimal for resting-state functional connectivity analyses.
To address these limitations, our proposed method achieves submillimeter resolution, layer specificity, brain-wide coverage, and a significantly shorter TR (<5 s) altogether. We believe this advancement provides a meaningful contribution to the field, enabling broader applicability of layer-fMRI at 3T.
(2) The authors implemented a sequence with lots of nice features. Including their own SMS EPI, diffusion bipolar pulses, eye-saturation bands, and they built their own reconstruction around it. This is not trivial. Only a few labs around the world have this level of engineering expertise. I applaud this technical achievement. However, I doubt that any of this is the right tool for layer-fMRI, nor does it represent an advancement for the field. In the thermal noise dominated regime of sub-millimeter fMRI (especially at 3T), it is established to use 3D readouts over 2D (SMS) readouts. While it is not trivial to implement SMS, the vendor implementations (as well as the CMRR and MGH implementations) are most widely applied across the majority of current fMRI studies already. The author's work on this does not serve any previous shortcomings in the field.
We would like to thank the reviewer for their comments and the recognition of the technical efforts in implementing our sequence. We would like to address the points raised:
(1) We completely agree that in-house implementation of existing techniques does not constitute an advancement for the field. We did not claim otherwise in the manuscript. Our focus was on the development of a method for brain-wide, layer-dependent resting-state functional connectivity at 3T, as mentioned in the response above.
(2) The reviewer stated that "it is established to use 3D readouts over 2D (SMS) readouts". This is a strong claim, and we believe it requires robust evidence to support it. While it is true that 3D readouts can achieve higher tSNR in certain regions, such as the central brain, as shown in the study by Vizioli et al. (ISMRM 2020 abstract; https://cds.ismrm.org/protected/20MProceedings/PDFfiles/3825.html?utm_source=chatgpt.com ), higher tSNR does not necessarily equate to improved detection power in fMRI studies. For instance, Le Ster et al. (PLOS ONE, 2019; https://doi.org/10.1371/journal.pone.0225286 ). demonstrated that while 3D EPI had higher tSNR in the central brain, SMS EPI produced higher t-scores in activation maps.
(3) When choosing between SMS EPI and 3D EPI, multiple factors should be taken into account, not just tSNR. For example, SMS EPI and 3D EPI differ in their sensitivity to motion and the complexity of motion correction. The choice between them depends on the specific research goals and practical constraints.
(4) We are open to different readout strategies, provided they can be demonstrated suitable to the research goals. In this study, we opted for 2D SMS primarily due to logistical considerations. This choice does not preclude the potential use of 3D readouts in the future if they are deemed more appropriate for the project objectives.
The mechanism to use bi-polar gradients to increase the localization specificity is doubtful to me. In my understanding, killing the intra-vascular BOLD should make it less specific. Also, the empirical data do not suggest a higher localization specificity to me.
We will elaborate the mechanism and reasoning in the later responses.
Embedding this work in the literature of previous methods is incomplete. Recent trends of vessel signal manipulation with ABC or VAPER are not mentioned. Comparisons with VASO are outdated and incorrect.
The reproducibility of the methods and the result is doubtful (see below).
In this revision, we updated the scan protocol and recollected the imaging data. Detailed explanations and revised results are provided in the later responses.
I don't think that this manuscript is in the top 50% of the 240 layer-fmri papers out there.
We respect the reviewer’s personal opinion. However, we can only address scientific comments or critiques.
Strengths:
See above. The authors developed their own SMS sequence with many features. This is important to the field. And does not leave sequence development work to view isolated monopoly labs. This work democratises SMS.
The questions addressed here are of high relevance to the field: getting tools with good sensitivity, user-friendly applicability, and locally specific brain activity mapping is an important topic in the field of layer-fMRI.
Weaknesses:
(1) I feel the authors need to justify why flow-crushing helps localization specificity. There is an entire family of recent papers that aim to achieve higher localization specificity by doing the exact opposite. Namely, MT or ABC fRMRI aims to increase the localization specificity by highlighting the intravascular BOLD by means of suppressing non-flowing tissue. To name a few:
Priovoulos, N., de Oliveira, I.A.F., Poser, B.A., Norris, D.G., van der Zwaag, W., 2023. Combining arterial blood contrast with BOLD increases fMRI intracortical contrast. Human Brain Mapping hbm.26227. https://doi.org/10.1002/hbm.26227.
Pfaffenrot, V., Koopmans, P.J., 2022. Magnetization Transfer weighted laminar fMRI with multi-echo FLASH. NeuroImage 119725. https://doi.org/10.1016/j.neuroimage.2022.119725
Schulz, J., Fazal, Z., Metere, R., Marques, J.P., Norris, D.G., 2020. Arterial blood contrast ( ABC ) enabled by magnetization transfer ( MT ): a novel MRI technique for enhancing the measurement of brain activation changes. bioRxiv. https://doi.org/10.1101/2020.05.20.106666
Based on this literature, it seems that the proposed method will make the vein problem worse, not better. The authors could make it clearer how they reason that making GE-BOLD signals more extra-vascular weighted should help to reduce large vein effects.
The proposed VN fMRI method employs VN gradients to selectively suppress signals from fast-flowing blood in large vessels. Although this approach may initially appear to diverge from the principles of CBV-based techniques (Chai et al., 2020; Huber et al., 2017a; Pfaffenrot and Koopmans, 2022; Priovoulos et al., 2023), which enhance sensitivity to vascular changes in arterioles, capillaries, and venules while attenuating signals from static tissue and large veins, it aligns with the fundamental objective of all layer-specific fMRI methods. Specifically, these approaches aim to maximize spatial specificity by preserving signals proximal to neural activation sites and minimizing contributions from distal sources, irrespective of whether the signals are intra- or extra-vascular in origin. In the context of intravascular signals, CBV-based methods preferentially enhance sensitivity to functional changes in small vessels (proximal components) while demonstrating reduced sensitivity to functional changes in large vessels (distal components). For extravascular signals, functional changes are a mixture of proximal and distal influences. While tissue oxygenation near neural activation sites represents a proximal contribution, extravascular signal contamination from large pial veins reflects distal effects that are spatially remote from the site of neuronal activity. CBV-based techniques mitigate this challenge by unselectively suppressing signals from static tissues, thereby highlighting contributions from small vessels. In contrast, the VN fMRI method employs a targeted suppression strategy, selectively attenuating signals from large vessels (distal components) while preserving those from small vessels (proximal components). Furthermore, the use of a 3T scanner and the inclusion of phase regression in the VN approach mitigates contamination from large pial veins (distal components) while preserving signals reflecting local tissue oxygenation (proximal components). By integrating these mechanisms, VN fMRI improves spatial specificity, minimizing both intravascular and extravascular contributions that are distal to neuronal activation sites. We have incorporated the responses into Discussion section.
The empirical evidence for the claim that flow crushing helps with the localization specificity should be made clearer. The response magnitude with and without flow crushing looks pretty much identical to me (see Fig, 6d).
In the new results in Figure 4, the application of VN gradients attenuated the bias towards pial surface. Consistent with the results in Figure 4, Figure 5 also demonstrated the suppression of macrovascular signal by VN gradients.
It's unclear to me what to look for in Fig. 5. I cannot discern any layer patterns in these maps. It's too noisy. The two maps of TE=43ms look like identical copies from each other. Maybe an editorial error?
In this revision, the original Figure 5 has been removed. However, we would like to clarify that the two maps with TE = 43 ms in the original Figure 5 were not identical. This can be observed in the difference map provided in the right panel of the figure.
The authors discuss bipolar crushing with respect to SE-BOLD where it has been previously applied. For SE-BOLD at UHF, a substantial portion of the vein signal comes from the intravascular compartment. So I agree that for SE-BOLD, it makes sense to crush the intravascular signal. For GE-BOLD however, this reasoning does not hold. For GE-BOLD (even at 3T), most of the vein signal comes from extravascular dephasing around large unspecific veins, and the bipolar crushing is not expected to help with this.
The reviewer’s statement that "most of the vein signal comes from extravascular dephasing around large unspecific veins" may hold true for 7T. However, at 3T, the susceptibility-induced Larmor frequency shift is reduced by 57%, and the extravascular contribution decreases by more than 35%, as shown by Uludağ et al. 2009 ( DOI: 10.1016/j.neuroimage.2009.05.051 ).
Additionally, according to the biophysical models (Ogawa et al., 1993; doi: 10.1016/S0006-3495(93)81441-3 ), the extravascular contamination from the pial surface is inversely proportional to the square of the distance from vessel. For a vessel diameter of 0.3 mm and an isotropic voxel size of 0.9 mm, the induced frequency shift is reduced by at least 36-fold at the next voxel. Notably, a vessel diameter of 0.3 mm is larger than most pial vessels. Theoretically, the extravascular effect contributes minimally to inter-layer dependency, particularly at 3T compared to 7T due to weaker susceptibility-related effects at lower field strengths. Empirically, as shown in Figure 7c, the results at M1 demonstrated that layer specificity can be achieved statistically with the application of VN gradients. We have incorporated this explanation into the Introduction and Discussion sections of the manuscript.
(2) The bipolar crushing is limited to one single direction of flow. This introduces a lot of artificial variance across the cortical folding pattern. This is not mentioned in the manuscript. There is an entire family of papers that perform layer-fmri with black-blood imaging that solves this with a 3D contrast preparation (VAPER) that is applied across a longer time period, thus killing the blood signal while it flows across all directions of the vascular tree. Here, the signal cruising is happening with a 2D readout as a "snap-shot" crushing. This does not allow the blood to flow in multiple directions.
VAPER also accounts for BOLD contaminations of larger draining veins by means of a tag-control sampling. The proposed approach here does not account for this contamination.
Chai, Y., Li, L., Huber, L., Poser, B.A., Bandettini, P.A., 2020. Integrated VASO and perfusion contrast: A new tool for laminar functional MRI. NeuroImage 207, 116358. https://doi.org/10.1016/j.neuroimage.2019.116358
Chai, Y., Liu, T.T., Marrett, S., Li, L., Khojandi, A., Handwerker, D.A., Alink, A., Muckli, L., Bandettini, P.A., 2021. Topographical and laminar distribution of audiovisual processing within human planum temporale. Progress in Neurobiology 102121. https://doi.org/10.1016/j.pneurobio.2021.102121
If I would recommend anyone to perform layer-fMRI with blood crushing, it seems that VAPER is the superior approach. The authors could make it clearer why users might want to use the unidirectional crushing instead.
We understand the reviewer’s concern regarding the directional limitation of bipolar crushing. As noted in the responses above, we have updated the bipolar gradient to include three orthogonal directions instead of a single direction. Furthermore, flow-related signal suppression does not necessarily require a longer time period. Bipolar diffusion gradients have been effectively used to nullify signals from fast-flowing blood, as demonstrated by Boxerman et al. (1995; DOI: 10.1002/mrm.1910340103). Their study showed that vessels with flow velocities producing phase changes greater than p radians due to bipolar gradients experience significant signal attenuation. The critical velocity for such attenuation can be calculated using the formula: 1/(2gGDd) where g is the gyromagnetic ratio, G is the gradient strength, d is the gradient pulse width and D is the time between the two bipolar gradient pulses. In the framework of Boxerman et al. at 1.5T, the critical velocity for b value of 10 s/mm<sup>2</sup> is ~8 mm/s, resulting in a ~30% reduction in functional signal. In our 3T study, b values of 6, 7, and 8 s/mm<sup>2</sup> correspond to critical velocities of 16.8, 15.2, and 13.9 mm/s, respectively. The flow velocities in capillaries and most venules remain well below these thresholds. Notably, in our VN fMRI sequences, bipolar gradients were applied in all three orthogonal directions, whereas in Boxerman et al.'s study, the gradients were applied only in the z-direction. Given the voxel dimensions of 3 × 3 × 7 mm<sup>3</sup> in the 1.5T study, vessels within a large voxel are likely oriented in multiple directions, meaning that only a subset of fast-flowing signals would be attenuated. Therefore, our approach is expected to induce greater signal reduction, even at the same b values as those used in Boxerman et al.'s study. We have incorporated this text into the Discussion section of the manuscript.
(3) The comparison with VASO is misleading.
The authors claim that previous VASO approaches were limited by TRs of 8.2s. The authors might be advised to check the latest literature of the last years.
Koiso et al. performed whole brain layer-fMRI VASO at 0.8mm at 3.9 seconds (with reliable activation), 2.7 seconds (with unconvincing activation pattern, though), and 2.3 (without activation).
Also, whole brain layer-fMRI BOLD at 0.5mm and 0.7mm has been previously performed by the Juelich group at TRs of 3.5s (their TR definition is 'fishy' though).
Koiso, K., Müller, A.K., Akamatsu, K., Dresbach, S., Gulban, O.F., Goebel, R., Miyawaki, Y., Poser, B.A., Huber, L., 2023. Acquisition and processing methods of whole-brain layer-fMRI VASO and BOLD: The Kenshu dataset. Aperture Neuro 34. https://doi.org/10.1101/2022.08.19.504502
Yun, S.D., Pais‐Roldán, P., Palomero‐Gallagher, N., Shah, N.J., 2022. Mapping of whole‐cerebrum resting‐state networks using ultra‐high resolution acquisition protocols. Human Brain Mapping. https://doi.org/10.1002/hbm.25855
Pais-Roldan, P., Yun, S.D., Palomero-Gallagher, N., Shah, N.J., 2023. Cortical depth-dependent human fMRI of resting-state networks using EPIK. Front. Neurosci. 17, 1151544. https://doi.org/10.3389/fnins.2023.1151544
We thank the reviewer for providing these references. While the protocol with a TR of 3.9 seconds in Koiso’s work demonstrated reasonable activation patterns, it was not tested for layer specificity. Given that higher acceleration factors (AF) can cause spatial blurring, a protocol should only be eligible for comparison if layer specificity is demonstrated.
Secondly, the TRs reported in Koiso’s study pertain only to either the VASO or BOLD acquisition, not the combined CBV-based contrast. To generate CBV-based images, both VASO and BOLD data are required, effectively doubling the TR. For instance, if the protocol with a TR of 3.9 seconds is used, the effective TR becomes approximately 8 seconds. The stable protocol used by Koiso et al. to acquire whole-brain data (94.08 mm along the z-axis) required 5.2 seconds for VASO and 5.1 seconds for BOLD, resulting in an effective TR of 10.3 seconds. The spatial resolution achieved was 0.84 mm isotropic.
Unfortunately, we could not find the Juelich paper mentioned by the reviewer.
To have a more comprehensive comparison, we collated relevant literature on brain-wide layer-specific fMRI. We defined brain-wide acquisition as imaging protocols that cover more than half of the human brain, specifically exceeding 55 mm along the superior-inferior axis. We identified five studies and summarized their scan parameters, including effective TR, coverage, and spatial resolution, in Table 1.
The authors are correct that VASO is not advised as a turn-key method for lower brain areas, incl. Hippocampus and subcortex. However, the authors use this word of caution that is intended for inexperienced "users" as a statement that this cannot be performed. This statement is taken out of context. This statement is not from the academic literature. It's advice for the 40+ user base that wants to perform layer-fMRI as a plug-and-play routine tool in neuroscience usage. In fact, sub-millimeter VASO is routinely being performed by MRI-physicists across all brain areas (including deep brain structures, hippocampus etc). E.g. see Koiso et al. and an overview lecture from a layer-fMRI workshop that I had recently attended: https://youtu.be/kzh-nWXd54s?si=hoIJjLLIxFUJ4g20&t=2401
In this revision, we decided to focus on cortico-cortical functional connectivity and have removed the LGN-related content. Consequently, the text mentioned by the reviewer was also removed. Nevertheless, we apologize if our original description gave the impression that functional mapping of deep brain regions using VASO is not feasible. The word of caution we used is based on the layer-fMRI blog ( https://layerfmri.com/2021/02/22/vaso_ve/ ) and reflects the challenges associated with this technique, as outlined by experts like Dr. Huber and Dr. Strinberg.
According to the information provided, including the video, functional mapping of the hippocampus and amygdala using VASO is indeed possible but remains technically challenging. The short arterial arrival times in these deep brain regions can complicate the acquisition, requiring RF inversion pulses to cover a wider area at the base of the brain. For example, as of 2023, four or more research groups were attempting to implement layer-fMRI VASO in the hippocampus. One such study at 3T required multiple inversion times to account for inflow effects, highlighting the technical complexity of these applications. This is the context in which we used the word of caution. We are not sure whether recent advancements like MAGEC VASO have improved its applicability. As of 2024, we have not identified any published VASO studies specifically targeting deep brain structures such as the hippocampus or amygdala. Therefore, it is difficult to conclude that “sub-millimeter VASO is routinely being performed by MRI physicists on deep brain structures such as the hippocampus.”
Thus, the authors could embed this phrasing into the context of their own method that they are proposing in the manuscript. E.g. the authors could state whether they think that their sequence has the potential to be disseminated across sites, considering that it requires slow offline reconstruction in Matlab?
We are enthusiastic about sharing our imaging sequence, provided its usefulness is conclusively established. However, it's important to note that without an online reconstruction capability, such as the ICE, the practical utility of the sequence may be limited. Unfortunately, we currently don’t have the manpower to implement the online reconstruction. Nevertheless, we are more than willing to share the offline reconstruction codes upon request.
Do the authors think that the results shown in Fig. 6c are suggesting turn-key acquisition of a routine mapping tool? In my humble opinion, it looks like random noise, with most of the activation outside the ROI (in white matter).
As we mentioned in the ‘general response’ in the beginning of the rebuttal, the POCS method for partial Fourier reconstruction caused the loss of functional feature, potentially accounting for the activation in white matter. In this revision, we have modified the pulse sequence, scan protocol and processing pipelines.
According to the results in Figure 4, stable activation in M1 was observed at the single-subject level across most scan protocols. Yet, the layer-dependent activation profiles in M1 were spatially unstable, irrespective of the application of VN gradients. This spatial instability is not entirely unexpected, as T2*-based contrast is inherently sensitive to various factors that perturb the magnetic field, such as eye movements, respiration, and macrovascular signal fluctuations. Furthermore, ICA-based artifact removal was intentionally omitted in Figure 4 to ensure fair comparisons between protocols, leaving residual artifacts unaddressed. Inconsistency in performing the button-pressing task across sessions may also have contributed to the observed variability. These results suggest that submillimeter-resolution fMRI may not yet be suitable for reliable individual-level layer-dependent functional mapping, unless group-level statistics are incorporated to enhance robustness. We have incorporated this text into the Limitation section of the manuscript.
(4) The repeatability of the results is questionable.
The authors perform experiments about the robustness of the method (line 620). The corresponding results are not suggesting any robustness to me. In fact, the layer profiles in Fig. 4c vs. Fig 4d are completely opposite. The location of peaks turns into locations of dips and vice versa.
The methods are not described in enough detail to reproduce these results.
The authors mention that their image reconstruction is done "using in-house MATLAB code" (line 634). They do not post a link to github, nor do they say if they share this code.
We thank the reviewer for the comments regarding reproducibility and data sharing. In response, we have revised the Methods section and elaborated on the technical details to improve clarity and reproducibility.
Regarding code sharing, we acknowledge that the current in-house MATLAB reconstruction code requires further refinement to improve its readability and usability. Due to limited manpower, we have not yet been able to complete this task. However, we are committed to making the code publicly available and will upload it to GitHub as soon as the necessary resources are available.
For data sharing, we face logistical challenges due to the large size of the dataset, which spans tens of terabytes. Platforms like OpenNeuro, for example, typically support datasets up to 10TB, making it difficult to share the data in its entirety. Despite this limitation, we are more than willing to share offline reconstruction codes and raw data upon request to facilitate reproducibility.
Regarding data robustness, we kindly refer the reviewer to our response to the previous comment, where we addressed these concerns in greater detail.
It is not trivial to get good phase data for fMRI. The authors do not mention how they perform the respective coil-combination.
No data are shared for reproduction of the analysis.
Obtaining phase data is relatively straightforward when the images are retrieved directly from raw data. For coil combination, we employed the adaptive coil combination approach described by (Walsh et al.; DOI: 10.1002/(sici)1522-2594(200005)43:5<682::aid-mrm10>3.0.co;2-g ) The MATLAB code for this implementation was developed by Dr. Diego Hernando and is publicly available at https://github.com/welton0411/matlab .
(5) The application of NODRIC is not validated.
Previous applications of NORDIC at 3T layer-fMRI have resulted in mixed success. When not adjusted for the right SNR regime it can result in artifactual reductions of beta scores, depending on the SNR across layers. The authors could validate their application of NORDIC and confirm that the average layer-profiles are unaffected by the application of NORDIC. Also, the NORDIC version should be explicitly mentioned in the manuscript.
Akbari, A., Gati, J.S., Zeman, P., Liem, B., Menon, R.S., 2023. Layer Dependence of Monocular and Binocular Responses in Human Ocular Dominance Columns at 7T using VASO and BOLD (preprint). Neuroscience. https://doi.org/10.1101/2023.04.06.535924
Knudsen, L., Guo, F., Huang, J., Blicher, J.U., Lund, T.E., Zhou, Y., Zhang, P., Yang, Y., 2023. The laminar pattern of proprioceptive activation in human primary motor cortex. bioRxiv. https://doi.org/10.1101/2023.10.29.564658
We appreciate the reviewer’s suggestion. To validate the application of NORDIC denoising in our study, we compared the BOLD activation maps before and after denoising in the visual and motor cortices, as well as the depth-dependent activation profiles in M1. These results are presented in Figure 3. The activation patterns in the denoised maps were consistent with those in the non-denoised maps but exhibited higher statistical significance. Notably, BOLD activation within M1 was only observed after NORDIC denoising, underscoring the necessity of this approach. Figure 3c shows the depth-dependent activation profiles in M1, highlighted by the green contours in Figure 3b. Both denoised and non-denoised profiles followed similar trends; however, as expected, the non-denoised profile exhibited larger confidence intervals compared to the NORDIC-denoised profile. These results confirm that NORDIC denoising enhances sensitivity without introducing distortions in the functional signal. The corresponding text has been incorporated into the Results section.
Regarding the implementation details of NORDIC denoising, the reconstructed images were denoised using a g-factor map (function name: NIFTI_NORDIC). The g-factor map was estimated from the image time series, and the input images were complex-valued. The width of the smoothing filter for the phase was set to 10, while all other hyperparameters were retained at their default values. This information has been integrated into the Methods section for clarity and reproducibility.
Reviewer #2 (Public Review):
This study developed a setup for laminar fMRI at 3T that aimed to get the best from all worlds in terms of brain coverage, temporal resolution, sensitivity to detect functional responses, and spatial specificity. They used a gradient-echo EPI readout to facilitate sensitivity, brain coverage and temporal resolution. The former was additionally boosted by NORDIC denoising and the latter two were further supported by parallel-imaging acceleration both in-plane and across slices. The authors evaluated whether the implementation of velocity-nulling (VN) gradients could mitigate macrovascular bias, known to hamper the laminar specificity of gradient-echo BOLD.
The setup allows for 0.9 mm isotropic acquisitions with large coverage at a reasonable TR (at least for block designs) and the fMRI results presented here were acquired within practical scan-times of 12-18 minutes. Also, in terms of the availability of the method, it is favorable that it benefits from lower field strength (additional time for VN-gradient implementation, afforded by longer gray matter T2*).
The well-known double peak feature in M1 during finger tapping was used as a test-bed to evaluate the spatial specificity. They were indeed able to demonstrate two distinct peaks in group-level laminar profiles extracted from M1 during finger tapping, which was largely free from superficial bias. This is rather intriguing as, even at 7T, clear peaks are usually only seen with spatially specific non-BOLD sequences. This is in line with their simple simulations, which nicely illustrated that, in theory, intravascular macrovascular signals should be suppressible with only minimal suppression of microvasculature when small b-values of the VN gradients are employed. However, the authors do not state how ROIs were defined making the validity of this finding unclear; were they defined from independent criteria or were they selected based on the region mostly expressing the double peak, which would clearly be circular? In any case, results are based on a very small sub-region of M1 in a single slice - it would be useful to see the generalizability of superficial-bias-free BOLD responses across a larger portion of M1.
We appreciate and understand the reviewer’s concerns. Given the small size of the hand knob region within M1 and its intersubject variability in location, defining this region automatically remains challenging. However, we applied specific criteria to minimize bias during the delineation of M1: 1) the hand knob region was required to be anatomically located in the precentral sulcus or gyrus; 2) it needed to exhibit consistent BOLD activation across the majority of testing conditions; and 3) the region was expected to show BOLD activation in the deep cortical layers under the condition of b = 0 and TE = 30 ms. Once the boundaries across cortical depth were defined, the gray matter boundaries of hand knob region were delineated based on the T1-weighted anatomical image and the cortical ribbon mask but excluded the BOLD activation map to minimize potential bias in manual delineation. Based on the new criteria, the resulting depth-dependent profiles, as shown in Figure 4, are no longer superficial-bias-free.
As repeatedly mentioned by the authors, a laminar fMRI setup must demonstrate adequate functional sensitivity to detect (in this case) BOLD responses. The sensitivity evaluation is unfortunately quite weak. It is mainly based on the argument that significant activation was found in a challenging sub-cortical region (LGN). However, it was a single participant, the activation map was not very convincing, and the demonstration of significant activation after considerable voxel-averaging is inadequate evidence to claim sufficient BOLD sensitivity. How well sensitivity is retained in the presence of VN gradients, high acceleration factors, etc., is therefore unclear. The ability of the setup to obtain meaningful functional connectivity results is reassuring, yet, more elaborate comparison with e.g., the conventional BOLD setup (no VN gradients) is warranted, for example by comparison of tSNR, quantification and comparison of CNR, illustration of unmasked-full-slice activation maps to compare noise-levels, comparison of the across-trial variance in each subject, etc. Furthermore, as NORDIC appears to be a cornerstone to enable submillimeter resolution in this setup at 3T, it is critical to evaluate its impact on the data through comparison with non-denoised data, which is currently lacking.
We appreciate the reviewer’s comments and acknowledge that the LGN results from a single participant were not sufficiently convincing. In this revision, we have removed the LGN-related results and focused on cortico-cortical FC. To evaluate data quality, we opted to present BOLD activation maps rather than tSNR, as high tSNR does not necessarily translate to high functional significance. In Figure 3, we illustrate the effect of NORDIC denoising, including activation maps and depth-dependent profiles. Figure 4 presents activation maps acquired under different TE and b values, demonstrating that VN gradients effectively reduce the bias toward the pial surface without altering the overall activation patterns. The results in Figure 4 and Figure 5 provide evidence that VN gradients retain sensitivity while reducing superficial bias. The ability of the setup to obtain meaningful FC results was validated through seed-based analyses, identifying distinct connectivity patterns in the superficial and deep layers of the primary motor cortex (M1), with significant inter-layer differences (see Figure 7). Further analyses with a seed in the primary sensory cortex (S1) demonstrated the reliability of the method (see Figure 8). For further details on the results, including the impact of VN gradients and NORDIC denoising, please refer to Figures 3 to 8 in the Results section.
Additionally, we acknowledge the limitations of our current protocol for submillimeter-resolution fMRI at the individual level. We found that robust layer-dependent functional mapping often requires group-level statistics to enhance reliability. This issue has been discussed in detail in the Limitations section.
The proposed setup might potentially be valuable to the field, which is continuously searching for techniques to achieve laminar specificity in gradient echo EPI acquisitions. Nonetheless, the above considerations need to be tackled to make a convincing case.
Reviewer #3 (Public Review):
Summary:
The authors are looking for a spatially specific functional brain response to visualise non-invasively with 3T (clinical field strength) MRI. They propose a velocity-nulled weighting to remove the signal from draining veins in a submillimeter multiband acquisition.
Strengths:
- This manuscript addresses a real need in the cognitive neuroscience community interested in imaging responses in cortical layers in-vivo in humans.
- An additional benefit is the proposed implementation at 3T, a widely available field strength.
Weaknesses:
- Although the VASO acquisition is discussed in the introduction section, the VN-sequence seems closer to diffusion-weighted functional MRI. The authors should make it more clear to the reader what the differences are, and how results are expected to differ. Generally, it is not so clear why the introduction is so focused on the VASO acquisition (which, curiously, lacks a reference to Lu et al 2013). There are many more alternatives to BOLD-weighted imaging for fMRI. CBF-weighted ASL and GRASE have been around for a while, ABC and double-SE have been proposed more recently.
The major distinction between diffusion-weighted fMRI (DW-fMRI) and our methodology lies in the b-value employed. DW-fMRI typically measures cellular swelling using b-values greater than 1000 s/mm<sup>2</sup> (e.g., 1800 s/mm(sup>2</sup>). In contrast, our VN-fMRI approach measures hemodynamic responses by employing smaller b-values specifically designed to suppress signals from fast-flowing draining veins rather than detecting microstructural changes.
Regarding other functional contrasts, we agree that more layer-dependent fMRI approaches should be mentioned. In this revision, we have expanded the Introduction section to include discussions of the double spin-echo approach and CBV-based methods, such as MT-weighted fMRI, VAPER, ABC, and CBF-based method ASL. Additionally, the reference to Lu et al. (2013) has been cited in the revised manuscript. The corresponding text has been incorporated into the Introduction section to provide a more comprehensive overview of alternative functional imaging techniques.
- The comparison in Figure 2 for different b-values shows % signal changes. However, as the baseline signal changes dramatically with added diffusion weighting, this is rather uninformative. A plot of t-values against cortical depth would be much more insightful.
- Surprisingly, the %-signal change for a b-value of 0 is not significantly different from 0 in the gray matter. This raises some doubts about the task or ROI definition. A finger-tapping task should reliably engage the primary motor cortex, even at 3T, and even in a single participant.
- The BOLD weighted images in Figure 3 show a very clear double-peak pattern. This contradicts the results in Figure 2 and is unexpected given the existing literature on BOLD responses as a function of cortical depth.
- Given that data from Figures 2, 3, and 4 are derived from a single participant each, order and attention affects might have dramatically affected the observed patterns. Especially for Figure 4, neither BOLD nor VN profiles are really different from 0, and without statistical values or inter-subject averaging, these cannot be used to draw conclusions from.
We appreciate the reviewer’s suggestions. In this revision, we have made significant updates to the participant recruitment, scan protocol, data processing, and M1 delineation. Please refer to the "General Responses" at the beginning of the rebuttal and the first response to Reviewer #2 for more details.
Previously, the variation in depth-dependent profiles was calculated across upscaled voxels within a specific layer. However, due to the small size of the hand knob region, the number of within-layer voxels was limited, resulting in inaccurate estimations of signal variation. In the revised manuscript, the signal was averaged within each layer before performing the GLM analysis, and signal variation was calculated using the temporal residuals. The technical details of these changes are described in the "Materials and Methods" section. Furthermore, while the initial submission used percentage signal change for the profiles of M1, the dramatic baseline fluctuations observed previously are no longer an issue after the modifications. For this reason, we retained the use of percentage signal change to present the depth-dependent profiles. After these adjustments, the profiles exhibited a bias toward the pial surface, particularly in the absence of VN gradients.
- In Figure 5, a phase regression is added to the data presented in Figure 4. However, for a phase regression to work, there has to be a (macrovascular) response to start with. As none of the responses in Figure 4 are significant for the single participant dataset, phase regression should probably not have been undertaken. In this case, the functional 'responses' appear to increase with phase regression, which is contra-intuitive and deserves an explanation.
We agreed with reviewer’s argument. In the revised results, the issues mentioned by the reviewer are largely diminished. The updated analyses demonstrate that phase regression effectively reduces superficial bias, as shown in Figures 4 and 5.
- Consistency of responses is indeed expected to increase by a removal of the more variable vascular component. However, the microvascular component is always expected to be smaller than the combination of microvascular + macrovascular responses. Note that the use of %signal changes may obscure this effect somewhat because of the modified baseline. Another expected feature of BOLD profiles containing both micro- and microvasculature is the draining towards the cortical surface. In the profiles shown in Figure 7, this is completely absent. In the group data, no significant responses to the task are shown anywhere in the cortical ribbon.
We agreed with reviewer’s comments. In the revised manuscript, the results have been substantially updated to addressing the concerns raised. The original Figure 7 is no longer relevant and has been removed.
- Although I'd like to applaud the authors for their ambition with the connectivity analysis, I feel that acquisitions that are so SNR starved as to fail to show a significant response to a motor task should not be used for brain wide directed connectivity analysis.
We appreciate the reviewer’s comments and share the concern about SNR limitations. In the updated results presented in Figure 5, the activation patterns in the visual cortex were consistent across TEs and b values. At the motor cortex, stable activation in M1 was observed at the single-subject level across most scan protocols. However, the layer-dependent activation profiles in M1 exhibited spatial instability, irrespective of the application of VN gradients. This spatial instability is not entirely unexpected, as T2*-based contrast is inherently sensitive to factors that perturb the magnetic field, such as eye movements, respiration, and macrovascular signal fluctuations. Additionally, ICA-based artifact removal was intentionally omitted in Figure 4 to ensure fair comparisons across protocols, leaving some residual artifacts unaddressed. Variability in task performance during button-pressing sessions may have further contributed to the observed inconsistencies.
Although these findings suggest that submillimeter-resolution fMRI may not yet be reliable for individual-level layer-dependent functional mapping, the group-level FC analyses can still yield robust results. In Figure 7, group-level statistics revealed distinct functional connectivity (FC) patterns associated with superficial and deep layers in M1. These FC maps exhibited significant differences between layers, demonstrating that VN fMRI enhances inter-layer independence. Additional FC analyses with a seed placed in S1 further validated these findings (see Figure 8).
The claim of specificity is supported by the observation of the double-peak pattern in the motor cortex, previously shown in multiple non-BOLD studies. However, this same pattern is shown in some of the BOLD weighted data, which seems to suggest that the double-peak pattern is not solely due to the added velocity nulling gradients. In addition, the well-known draining towards the cortical surface is not replicated for the BOLD-weighted data in Figures 3, 4, or 7. This puts some doubt about the data actually having the SNR to draw conclusions about the observed patterns.
We appreciate the reviewer’s comments. In the updated results, the efficacy of the VN gradients is evident near the pial surface, as shown in Figures 4 and 5. In Figure 4, comparing the second and third columns (b = 0 and b = 6 s/mm<sup>2</sup>, respectively, at TE = 38 ms), the percentage signal change in the superficial layers is generally lower with b = 6 s/mm<sup>2</sup> than with b = 0. This indicates that VN gradient-induced signal suppression is more pronounced in the superficial layers. Additionally, in Figure 5, the VN gradients effectively suppressed macrovascular signals as highlighted by the blue circles. These observations support the role of VN gradients in enhancing specificity by reducing superficial bias and macrovascular contamination. Furthermore, bias towards cortical surface was observed in the updated results in Figure 4.
Recommendations for the authors:
Reviewer #2 (Recommendations For The Authors):
(1) L141: "depth dependent" is slightly misleading here. It could be misunderstood to suggest that the authors are assessing how spatial specificity varies as a function of depth. Rather, they are assessing spatial specificity based on depth-dependent responses (double peak feature). Perhaps "layer-dependent spatial specificity" could be substituted with laminar specificity?
We thank the reviewer for the suggestion. The term “depth dependent” has been replaced by “layer dependent” in the revised manuscript.
(2) L146-149: these do not validate spatial specificity.
The original text is removed.
(3) L180: Maybe helpful to describe what the b-value is to assist unfamiliar readers.
We have clarified the b-value as “the strength of the bipolar diffusion gradients” where it is first mentioned in the manuscript.
(4) Figure 1B: I think it would be appropriate with a sentence of how the authors define micro/macrovasculature. Figure 1B seems to suggest that large ascending veins are considered microvascular which I believe is a bit unconventional. Nevertheless, as long as it is clearly stated, it should be fine.
In our context, macrovasculature refers to vessels that are distal to neural activation sites and contribute to extravascular contamination. These vessels are typically larger in size (e.g., > 0.1 mm in diameter) and exhibit faster flow rates (e.g., > 10 mm/s).
(5) I think the authors could be more upfront with the point about non-suppressed extravascular effects from macrovasculature, which was briefly mentioned in the discussion. It could already be highlighted in the introduction or theory section.
We thank the reviewer’s suggestions. We have expanded the discussion of extravascular effects from macrovasculature in both the Introduction (5th paragraph) and Discussion (3rd paragraph) sections.
(6) The phase regression figure feels a bit misplaced to me. If the authors agree: rather than showing the TE-dependency of the effect of phase regression, it may be more relevant for the present study to compare the conventional setup with phase regression, with the VN setup without phase regression. I.e., to show how the proposed setup compares to existing 3T laminar fMRI studies.
In this revision, both the TE-dependent and VN-dependent effects of phase regression were investigated. The results in Figure 4 and Figure 5 demonstrated that phase regression effectively suppresses macrovascular contributions primarily near the gray matter/CSF boundary, irrespective of TE or the presence of VN gradients.
(7) L520: It might be beneficial to also cite the large body of other laminar studies showing the double peak feature to underscore that it is highly robust, which increases its relevance as a test-bed to assess spatial specificity.
We agreed. More literatures have been cited (Chai et al., 2020; Huber et al., 2017a; Knudsen et al., 2023; Priovoulos et al., 2023).
(8) L557: The argument that only one participant was assessed to reduce inter-subject variability is hard to buy. If significant variability exists across subjects, this would be highly relevant to the authors and something they would want to capture.
We thank the reviewer for the suggestions. In this revision, we have increased the number of participants to 4 for protocol development and 14 for resting-state functional connectivity analysis, allowing us to better assess and account for inter-subject variability.
(9) L637: add download link and version number.
The download link has been added as requested. The version number is not applicable.
(10) L638: How was the phase data coil-combined?
The reconstructed multi-channel data, which were of complex values, were combined using the adaptive combination method (Walsh et al.; DOI: 10.1002/(sici)1522-2594(200005)43:5<682::aid-mrm10>3.0.co;2-g). The MATLAB code for this implementation was developed by Dr. Diego Hernando and is publicly available at https://github.com/welton0411/matlab . The phase data were then extracted using the MATLAB function ‘angle’.
(11) L639: Why was the smoothing filter parameter changed (other parameters were default)?
The smoothing filter parameter was set based on the suggestion provided in the help comments of the NIFTI_NORDIC function:
function NIFTI_NORDIC(fn_magn_in,fn_phase_in,fn_out,ARG)
% fMRI
%
% ARG.phase_filter_width=10;
In other words, we simply followed the recommendation outlined in the NIFTI_NORDIC function’s documentation.
(12) I assume the phase data was motion corrected after transforming to real and imaginary components and using parameters estimated from magnitude data? Maybe add a few sentences about this.
Prior to phase regression, the time series of real and imaginary components were subjected to motion correction, followed by phase unwrapping. The phase regression was incorporated early in the data processing pipeline to minimize the discrepancy in data processing between magnitude and phase images (Stanley et al., 2021).
(13) Was phase regression applied with e.g., a deming model, which accounts for noise on both the x and y variable? In my experience, this makes a huge difference compared with regular OLS.
We appreciate the reviewer’s insightful comment. We are aware that the noise present in both magnitude and phase data therefore linear Deming regression would be a good fit to phase regression (Stanley et al., 2021). To perform Deming regression, however, the ratio of magnitude error variance to phase error variance must be predefined. In our initial tests, we found that the regression results were sensitive to this ratio. To avoid potential confounding, we opted to use OLS regression for the current analysis. However, we agreed Deming model could enhance the efficacy of phase regression if the ratio could be determined objectively and properly.
(14) Figure 2: What is error bar reflecting? I don't think the across-voxel error, as also used in Figure 4, is super meaningful as it assumes the same response of all voxels within a layer (might be alright for such a small ROI). Would it be better to e.g. estimate single-trial response magnitude (percent signal change) and assess variability across? Also, it is not obvious to me why b=30 was chosen. The authors argue that larger values may kill signal, but based on this Figure in isolation, b=48 did not have smaller response magnitudes (larger if anything).
We agreed with the reviewer’s opinion on the across-voxel error. In the revised manuscript, the signal was averaged within each layer before performing the GLM analysis, and signal variation was calculated using the temporal residuals. The technical details of these changes are described in the "Materials and Methods" section.
Additionally, the bipolar diffusion gradients were modified from a single direction to three orthogonal directions. As a result, the questions and results related to b=30 or b=48 are no longer applicable.
(15) Figure 5: would be informative to quantify the effect of phase regression over a large ROI and evaluate reduction in macrovascular influence from superficial bias in laminar profiles.
We appreciate the reviewer’s suggestion. In the revised manuscript, the reduction in macrovascular influence from superficial bias across a large ROI is displayed in Figure 5. Additionally, the impact on laminar profiles is demonstrated in Figure 4.
(16) L406-408: What kind of robustness?
We acknowledge that describing the protocol as “robust” was an overstatement. The updated results indicate that the current protocol for submillimeter fMRI may not yet be suitable for reliable individual-level layer-dependent functional mapping. However, group-level functional connectivity (FC) analyses demonstrated clear layer-specific distinctions with VN fMRI, which were not evident in conventional fMRI. These findings highlight the enhanced layer specificity achievable with VN fMRI.
(17) Figure 8: I think C) needs pointers to superficial, middle, and deep layers? Why is it not in the same format as in Figure 9C? The discussion of the FC results could benefit from more references supporting that these observations are in line with the literature.
In the revised results, the layer pooling shown in Figure 9c has been removed, making the question regarding format alignment no longer applicable. Additionally, references supporting the FC results have been added to the revised Discussion section (7th paragraph).
(18) L456-457: But correlation coefficients may also be biased by different CNR across layers.
That is correct. In the updated FC results in Figure 7 to 9, we used group-level statistics rather than correlation coefficients.
Reviewer #3 (Recommendations For The Authors):
The results in Figure 2-6 should be repeated over, or averaged over, a (small) group of participants. N=6 is usual in this field. I would seriously reconsider the multiband acceleration - the acquisition seemingly cannot support the SNR hit.
A few more specific points are given below:
(1) Abstract: The sentence about LGN in the abstract came for me out of the blue - why would LGN be important here, it's not even a motor network node? Perhaps the aims of the study should be made more clear - if it's about networks as suggested earlier then a network analysis result would be expected too. Expanding the directed FC findings would improve the logical flow of the abstract. Given the many concerns, removing the connectivity analysis altogether would also be an option.
We thank the reviewer for the suggestions. The LGN-related results indeed diluted the focus of this study and have been completely removed in this revision.
(2) Line 105: in addition to the VASO method, ..
The corresponding text has been revised, and as a result, the reviewer’s suggestion is no longer applicable.
(3) If out of the set MB 4 / 5 / 6 MB4 was best, why did the authors not continue with a comparison including MB3 and MB2? It seems to me unlikely that the MB4 acquisition is actually optimal.
Results: We appreciate the reviewer’s suggestions. In this revision, we decreased the MB factor to 3, as it allowed us to increase the in-plane acceleration rate to 3, thereby shortening the TE. The resulting sensitivity for both individual and group-level results is detailed in earlier responses, such as the response to Q16 for Reviewer #2.
(4) The formatting of the references is occasionally flawed, including first names and/or initials. Please consider using a reliable reference manager.
We used Zotero as our reference manager in this revision to ensure consistency and accuracy. The references have been formatted according to the APA style.
(5) In the caption of Figure 5, corrected and uncorrected p values are identical. What multiple comparisons correction was made here? A multiple comparisions over voxels (as is standard) would usually lead to a cut-off ~z=3.2. That would remove most of the 'responses' shown in figure 5.
We appreciate the reviewer’s comment. The original results presented in Figure 5 have been removed in the revised manuscript, making this comment no longer applicable.
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Reviewer #2 (Public review):
FOXP3 has been known to form diverse complexes with different transcription factors and enzymes responsible for epigenetic modifications, but how extracellular signals timely regulate FOXP3 complex dynamics remains to be fully understood. Histone H3K4 tri-methylation (H3K4me3) and CXXC finger protein 1 (CXXC1), which is required to regulate H3K4me3, also remain to be fully investigated in Treg cells. Here, Meng et al. performed a comprehensive analysis of H3K4me3 CUT&Tag assay on Treg cells and a comparison of the dataset with the FOXP3 ChIP-seq dataset revealed that FOXP3 could facilitate the regulation of target genes by promoting H3K4me3 deposition. Moreover, CXXC1-FOXP3 interaction is required for this regulation. They found that specific knockdown of Cxxc1 in Treg leads to spontaneous severe multi-organ inflammation in mice and that Cxxc1-deficient Treg exhibits enhanced activation and impaired suppression activity. In addition, they have also found that CXXC1 shares several binding sites with FOXP3 especially on Treg signature gene loci, which are necessary for maintaining homeostasis and identity of Treg cells.
Comments on revisions:
The authors have fully addressed the reviewers' comments and questions.
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Author response:
The following is the authors’ response to the original reviews.
Reviewer #1 (Public review):
Summary:
This work investigated the role of CXXC-finger protein 1 (CXXC1) in regulatory T cells. CXXC1-bound genomic regions largely overlap with Foxp3-bound regions and regions with H3K4me3 histone modifications in Treg cells. CXXC1 and Foxp3 interact with each other, as shown by co-immunoprecipitation. Mice with Treg-specific CXXC1 knockout (KO) succumb to lymphoproliferative diseases between 3 to 4 weeks of age, similar to Foxp3 KO mice. Although the immune suppression function of CXXC1 KO Treg is comparable to WT Treg in an in vitro assay, these KO Tregs failed to suppress autoimmune diseases such as EAE and colitis in Treg transfer models in vivo. This is partly due to the diminished survival of the KO Tregs after transfer. CXXC1 KO Tregs do not have an altered DNA methylation pattern; instead, they display weakened H3K4me3 modifications within the broad H3K4me3 domains, which contain a set of Treg signature genes. These results suggest that CXXC1 and Foxp3 collaborate to regulate Treg homeostasis and function by promoting Treg signature gene expression through maintaining H3K4me3 modification.
Strengths:
Epigenetic regulation of Treg cells has been a constantly evolving area of research. The current study revealed CXXC1 as a previously unidentified epigenetic regulator of Tregs. The strong phenotype of the knockout mouse supports the critical role CXXC1 plays in Treg cells. Mechanistically, the link between CXXC1 and the maintenance of broad H3K4me3 domains is also a novel finding.
Weaknesses:
(1) It is not clear why the authors chose to compare H3K4me3 and H3K27me3 enriched genomic regions. There are other histone modifications associated with transcription activation or repression. Please provide justification.
Thank you for highlighting this important point. We chose to focus on H3K4me3 and H3K27me3 enriched genomic regions because these histone modifications are well-characterized markers of transcriptional activation and repression, respectively. H3K4me3 is predominantly associated with active promoters, while H3K27me3 marks repressed chromatin states, particularly in the context of gene regulation at promoters. This duality provides a robust framework for investigating the balance between transcriptional activation and repression in Treg cells. While histone acetylation, such as H3K27ac, is linked to enhancer activity and transcriptional elongation, our focus was on promoter-level regulation, where H3K4me3 and H3K27me3 are most relevant. Although other histone modifications could provide additional insights, we chose to focus on these two to maintain clarity and feasibility in our analysis. We have revised the text accordingly; please refer to Page 18, lines 353-356.
(2) It is not clear what separates Clusters 1 and 3 in Figure 1C. It seems they share the same features.
We apologize for not clarifying these clusters clearly. Cluster 1 and 3 are both H3K4me3 only group, with H3K4me3 enrichment and gene expression levels being higher in Cluster 1. At first, we divided the promoters into four categories because we wanted to try to classify them into four categories: H3K4me3 only, H3K27me3 only, H3K4me3-H3K27me3 co-occupied, and None. However, in actual classification, we could not distinguish H3K4me3-H3K27me3 co-occupied group. Instead, we had two categories of H3K4me3 only, with cluster 1 having a higher enrichment level for H3K4me3 and gene expression levels.
(3) The claim, "These observations support the hypothesis that FOXP3 primarily functions as an activator by promoting H3K4me3 deposition in Treg cells." (line 344), seems to be a bit of an overstatement. Foxp3 certainly can promote transcription in ways other than promoting H3K3me3 deposition, and it also can repress gene transcription without affecting H3K27me3 deposition. Therefore, it is not justified to claim that promoting H3K4me3 deposition is Foxp3's primary function.
Thank you for your insightful feedback. We agree that the statement in line 344 may have overstated the role of FOXP3 in promoting H3K4me3 deposition as its primary function. As you pointed out, FOXP3 is indeed a multifaceted transcription factor that regulates gene expression through various mechanisms. It can promote transcription independent of H3K4me3 deposition, as well as repress transcription without directly influencing H3K27me3 levels.
To more accurately reflect the broader regulatory functions of FOXP3, we have revised the manuscript. The updated text (Page 19, lines 385-388) now reads:
"These findings collectively support the conclusion that FOXP3 contributes to transcriptional activation in Treg cells by promoting H3K4me3 deposition at target loci, while also regulating gene expression directly or indirectly through other epigenetic modifications.
(4) For the in vitro suppression assay in Figure S4C, and the Treg transfer EAE and colitis experiments in Figure 4, the Tregs should be isolated from Cxxc1 fl/fl x Foxp3 cre/wt female heterozygous mice instead of Cxxc1 fl/fl x Foxp3 cre/cre (or cre/Y) mice. Tregs from the homozygous KO mice are already activated by the lymphoproliferative environment and could have vastly different gene expression patterns and homeostatic features compared to resting Tregs. Therefore, it's not a fair comparison between these activated KO Tregs and resting WT Tregs.
Thank you for raising this insightful point regarding the potential activation status of Treg cells in homozygous knockout mice. To address this concern, we performed additional experiments using Treg cells isolated from Foxp3<sup>Cre/+</sup>Cxxc1<sup>fl/fl</sup> (hereafter referred to as “het-KO”) female mice and their littermate controls, Foxp3<sup>Cre/+</sup>Cxxc1<sup>fl/+</sup> (referred to as “het-WT”) mice.
The results of these new experiments are now included in the manuscript (Page25, lines 507–509, Figure 6E and Figure S6A-E):
(1) In the in vitro suppression assay, Treg cells from het-KO mice exhibited reduced suppressive function compared to het-WT Treg cells. This finding underscores the intrinsic defect in Treg cells suppressive capacity attributable to the loss of one Cxxc1 allele.
(2) In the experimental autoimmune encephalomyelitis (EAE) model, Treg cells isolated from het-KO mice also demonstrated impaired suppressive function.
(5) The manuscript didn't provide a potential mechanism for how CXXC1 strengthens broad H3K4me3-modified genomic regions. The authors should perform Foxp3 ChIP-seq or Cut-n-Taq with WT and Cxxc1 cKO Tregs to determine whether CXXC1 deletion changes Foxp3's binding pattern in Treg cells.
Thank you for raising this important point. To address your suggestion, we performed CUT&Tag experiments and found that Cxxc1 deletion does not alter FOXP3 binding patterns in Treg cells. Most FOXP3-bound regions in WT Treg cells were similarly enriched in KO Treg cells, indicating that Cxxc1 deficiency does not impair FOXP3’s DNA-binding ability. These results have been added to the revised manuscript (Page 28, lines 567-575, Figure S8A-B) and are further discussed in the Discussion (Pages 28-29, lines 581-587).
Reviewer #2 (Public review):
FOXP3 has been known to form diverse complexes with different transcription factors and enzymes responsible for epigenetic modifications, but how extracellular signals timely regulate FOXP3 complex dynamics remains to be fully understood. Histone H3K4 tri-methylation (H3K4me3) and CXXC finger protein 1 (CXXC1), which is required to regulate H3K4me3, also remain to be fully investigated in Treg cells. Here, Meng et al. performed a comprehensive analysis of H3K4me3 CUT&Tag assay on Treg cells and a comparison of the dataset with the FOXP3 ChIP-seq dataset revealed that FOXP3 could facilitate the regulation of target genes by promoting H3K4me3 deposition.
Moreover, CXXC1-FOXP3 interaction is required for this regulation. They found that specific knockdown of Cxxc1 in Treg leads to spontaneous severe multi-organ inflammation in mice and that Cxxc1-deficient Treg exhibits enhanced activation and impaired suppression activity. In addition, they have also found that CXXC1 shares several binding sites with FOXP3 especially on Treg signature gene loci, which are necessary for maintaining homeostasis and identity of Treg cells.
The findings of the current study are pretty intriguing, and it would be great if the authors could fully address the following comments to support these interesting findings.
Major points:
(1) There is insufficient evidence in the first part of the Results to support the conclusion that "FOXP3 functions as an activator by promoting H3K4Me3 deposition in Treg cells". The authors should compare the results for H3K4Me3 in FOXP3-negative conventional T cells to demonstrate that at these promoter loci, FOXP3 promotes H3K4Me3 deposition.
Thank you for this insightful comment. We have already performed additional experiments comparing H3K4Me3 levels between FOXP3-positive Treg cells and FOXP3-negative conventional T cells (Tconv). Please refer to Pages 18, lines 361-368, and Figure 1C and Figure S1C for the results. Our results show that H3K4Me3 abundance is higher at many Treg-specific gene loci in Treg cells compared to Tconv cells. This supports our conclusion that FOXP3 promotes H3K4Me3 deposition at these loci.
(2) In Figure 3 F&G, the activation status and IFNγ production should be analyzed in Treg cells and Tconv cells separately rather than in total CD4+ T cells. Moreover, are there changes in autoantibodies and IgG and IgE levels in the serum of cKO mice?
Thank you for your valuable suggestions. In response to your comment, we reanalyzed the data in Figures 3F and 3G to assess the activation status and IFN-γ production in Tconv cells. The updated analysis revealed that Cxxc1 deletion in Treg cells leads to increased activation and IFN-γ production in Tconv cells. Additionally, we corrected the analysis of IL-17A and IL-4 expression, which were upregulated in Tconv cells. These updated results are now included in the revised manuscript (Page 21, lines 429-431, Figure 3I and Figure S3E-F).
Additionally, we examined autoantibodies and immunoglobulin levels in the serum of Cxxc1 cKO mice. Our data show a significant increase in serum IgG levels, accompanied by elevated IgG autoantibodies, indicating heightened autoimmune responses. In contrast, serum IgE levels remained largely unchanged. The results are detailed in the revised manuscript (Page 21, lines 421-423, Figure 3E and Figure S3B).
(3) Why did Cxxc1-deficient Treg cells not show impaired suppression than WT Treg during in vitro suppression assay, despite the reduced expression of Treg cell suppression assay -associated markers at the transcriptional level demonstrated in both scRNA-seq and bulk RNA-seq?
Thank you for your thoughtful comment. The absence of impaired suppression in Cxxc1-deficient Treg cells from homozygous knockout (KO) mice during the in vitro suppression assay, despite the reduced expression of Treg-associated markers at the transcriptional level (as demonstrated by scRNA-seq), can likely be explained by the activated state of these Treg cells. In homozygous KO mice, Treg cells are already activated due to the lymphoproliferative environment, resulting in gene expression patterns that differ from those of resting Treg cells. This pre-activation may obscure the effect of Cxxc1 deletion on their suppressive function in vitro.
To address this limitation, we used heterozygous Foxp3<sup>Cre/+</sup>Cxxc1<sup>fl/fl</sup> (het-KO) female mice, along with their littermate controls, Foxp3<sup>Cre/+</sup>Cxxc1<sup>fl/+</sup> (het-WT) mice. In these heterozygous mice, we observed an impairment in Treg cell suppressive function in vitro, which was accompanied by the downregulation of several key Treg-associated genes, as confirmed by RNA-Seq analysis.
These updated findings, based on the use of het-KO mice, are now incorporated into the revised manuscript (Page 25, lines 507–509, Figure 6E).
(4) Is there a disease in which Cxxc1 is expressed at low levels or absent in Treg cells? Is the same immunodeficiency phenotype present in patients as in mice?
This is indeed a very meaningful and intriguing question, and we are equally interested in understanding whether low or absent Cxxc1 expression in Treg cells is associated with any human diseases. However, despite an extensive review of the literature and available data, we found no reports linking Cxxc1 deficiency in Treg cells to immunodeficiency phenotypes in patients comparable to those observed in mice.
Reviewer #3 (Public review):
In the report entitled "CXXC-finger protein 1 associates with FOXP3 to stabilize homeostasis and suppressive functions of regulatory T cells", the authors demonstrated that Cxxc1-deletion in Treg cells leads to the development of severe inflammatory disease with impaired suppressive function. Mechanistically, CXXC1 interacts with Foxp3 and regulates the expression of key Treg signature genes by modulating H3K4me3 deposition. Their findings are interesting and significant. However, there are several concerns regarding their analysis and conclusions.
Major concerns:
(1) Despite cKO mice showing an increase in Treg cells in the lymph nodes and Cxxc1-deficient Treg cells having normal suppressive function, the majority of cKO mice died within a month. What causes cKO mice to die from severe inflammation?
Considering the results of Figures 4 and 5, a decrease in the Treg cell population due to their reduced proliferative capacity may be one of the causes. It would be informative to analyze the population of tissue Treg cells.
Thank you for your insightful observation regarding the mortality of cKO mice despite increased Treg cells in lymph nodes and the normal suppressive function of Cxxc1-deficient Treg cells.
As suggested, we hypothesized that the reduction of tissue-resident Treg cells could be a key factor. Additional experiments revealed a significant decrease in Treg cell populations in the small intestine lamina propria (LPL), liver, and lung of cKO mice. These findings highlight the critical role of tissue-resident Treg cells in preventing systemic inflammation.
This reduction aligns with Figures 4 and 5, which demonstrate impaired proliferation and survival of Cxxc1-deficient Treg cells. Together, these defects lead to insufficient Treg populations in peripheral tissues, escalating localized inflammation into systemic immune dysregulation and early mortality.
These additional results have been incorporated into the revised manuscript (Page21, lines 424-427, Figure 3G and Figure S3C).
(2) In Figure 5B, scRNA-seq analysis indicated that the Mki67+ Treg subset is comparable between WT and Cxxc1-deficient Treg cells. On the other hand, FACS analysis demonstrated that Cxxc1-deficient Treg shows less Ki-67 expression compared to WT in Figure 5I. The authors should explain this discrepancy.
Thank you for pointing out the apparent discrepancy between the scRNA-seq and FACS analyses regarding Ki-67 expression in Cxxc1-deficient Treg cells.
In Figure 5B, the scRNA-seq analysis identified the Mki67+ Treg subset as comparable between WT and Cxxc1-deficient Treg cells. This finding reflects the overall proportion of cells expressing Mki67 transcripts within the Treg population. In contrast, the FACS analysis in Figure 5I specifically measures Ki-67 protein levels, revealing reduced expression in Cxxc1-deficient Treg cells compared to WT.
To resolve this discrepancy, we performed additional analyses of the scRNA-seq data to directly compare the expression levels of Mki67 mRNA between WT and Cxxc1-deficient Treg cells. The results revealed a consistent reduction in Mki67 transcript levels in Cxxc1-deficient Treg cells, aligning with the reduced Ki-67 protein levels observed by FACS.
These new analyses have been included in the revised manuscript (Author response image 1) to clarify this point and demonstrate consistency between the scRNA-seq and FACS data.
Author response image 1.
Violin plots displaying the expression levels of Mki67 in T<sub>reg</sub> cells from Foxp3<sup>cre</sup> and Foxp3<sup>cre</sup>Cxxc1<sup>fl/fl</sup> mice.
In addition, the authors concluded on line 441 that CXXC1 plays a crucial role in maintaining Treg cell stability. However, there appears to be no data on Treg stability. Which data represent the Treg stability?
Thank you for your valuable comment. We agree that our wording in line 441 may have been too conclusive. Our data focus on the impact of Cxxc1 deficiency on Treg cell homeostasis and transcriptional regulation, rather than directly measuring Treg cell stability. Specifically, the downregulation of Treg-specific suppressive genes and upregulation of pro-inflammatory markers suggest a shift in Treg cell function, which points to disrupted homeostasis rather than stability.
We have revised the manuscript to clarify that CXXC1 plays a crucial role in maintaining Treg cell function and homeostasis, rather than stability (Page 24, lines 489-491).
(3) The authors found that Cxxc1-deficient Treg cells exhibit weaker H3K4me3 signals compared to WT in Figure 7. This result suggests that Cxxc1 regulates H3K4me3 modification via H3K4 methyltransferases in Treg cells. The authors should clarify which H3K4 methyltransferases contribute to the modulation of H3K4me3 deposition by Cxxc1 in Treg cells.
We appreciate the reviewer’s insightful comment regarding the role of H3K4 methyltransferases in regulating H3K4me3 deposition by CXXC1 in Treg cells.
CXXC1 has been reported to function as a non-catalytic component of the Set1/COMPASS complex, which includes the H3K4 methyltransferases SETD1A and SETD1B—key enzymes responsible for H3K4 trimethylation(1-4). Based on these findings, we propose that CXXC1 modulates H3K4me3 levels in Treg cells by interacting with and stabilizing the activity of the Set1/COMPASS complex.
These revisions are further discussed in the Discussion (Page 30-31, lines 624-632).
Furthermore, it would be important to investigate whether Cxxc1-deletion alters Foxp3 binding to target genes.
Thank you for raising this important point. To address your suggestion, we performed CUT&Tag experiments and found that Cxxc1 deletion does not alter FOXP3 binding patterns in Treg cells. Most FOXP3-bound regions in WT Treg cells were similarly enriched in KO Treg cells, indicating that Cxxc1 deficiency does not impair FOXP3’s DNA-binding ability. These results have been added to the revised manuscript (Page 28, lines 567-575, Figure S8A-B) and are further discussed in the Discussion (Pages 28-29, lines 581-587).
(4) In Figure 7, the authors concluded that CXXC1 promotes Treg cell homeostasis and function by preserving the H3K4me3 modification since Cxxc1-deficient Treg cells show lower H3K4me3 densities at the key Treg signature genes. Are these Cxxc1-deficient Treg cells derived from mosaic mice? If Cxxc1-deficient Treg cells are derived from cKO mice, the gene expression and H3K4me3 modification status are inconsistent because scRNA-seq analysis indicated that expression of these Treg signature genes was increased in Cxxc1-deficient Treg cells compared to WT (Figure 5F and G).
Thank you for your insightful comment. To clarify, the Cxxc1-deficient Treg cells analyzed for H3K4me3 modifications in Figure 7 were derived from Cxxc1 conditional knockout (cKO) mice, not mosaic mice.
Regarding the apparent inconsistency between reduced H3K4me3 levels and the increased expression of Treg signature genes observed in scRNA-seq analysis (Figure 5F and G), we believe this discrepancy can be attributed to distinct mechanisms regulating gene expression. H3K4me3 is an epigenetic mark that facilitates chromatin accessibility and transcriptional regulation, reflecting upstream chromatin dynamics. However, gene expression levels are influenced by a combination of factors, including transcriptional activators, downstream compensatory mechanisms, and the inflammatory environment in cKO mice.
The upregulation of Treg signature genes in scRNA-seq data likely reflects an activated or pro-inflammatory state of Cxxc1-deficient Treg cells in response to systemic inflammation, as previously described in the manuscript. This contrasts with the intrinsic reduction in H3K4me3 levels at these loci, indicating a loss of epigenetic regulation by CXXC1.
To further support this interpretation, RNA-seq analysis of Treg cells from Foxp3<sup>Cre/+</sup> Cxxc1<sup>fl/fl</sup> (“het-KO”) and their littermate Foxp3<sup>Cre/+</sup> Cxxc1<sup>fl/+</sup> (“het-WT”) female mice (Figure S6C) revealed a significant reduction in key Treg signature genes such as Icos, Ctla4, Tnfrsf18, and Nt5e in het-KO Treg cells. These results align with the diminished H3K4me3 modifications observed in cKO Treg cells, further underscoring the role of CXXC1 as an epigenetic regulator.
In summary, while the gene expression changes observed in scRNA-seq may reflect adaptive responses to inflammation, the reduced H3K4me3 modifications directly highlight the critical role of CXXC1 in maintaining the epigenetic landscape essential for Treg cell homeostasis and function.
Recommendations for the authors:
Reviewer #1 (Recommendations for the authors):
In Figure 7E, the y-axis scale for H3K4me3 peaks at the Ctla4 locus should be consistent between WT and cKO samples.
We thank the reviewer for pointing out the inconsistency in the y-axis scale for the H3K4me3 peaks at the Ctla4 locus in Figure 7E. We have carefully revised the figure to ensure that the y-axis scale is now consistent between the WT and cKO samples.
We appreciate the reviewer’s attention to this detail, as it enhances the rigor of the data presentation. Please find the updated Figure 7E in the revised manuscript.
Reviewer #2 (Recommendations for the authors):
In lines 455 and 466, the name of Treg signature markers validated by flow cytometry should be written as protein name and capitalized.
Thank you for pointing this out. We have carefully reviewed lines 455 and 466 and have revised the text to ensure that the Treg signature markers validated by flow cytometry are referred to using their protein names, with proper capitalization.
Reviewer #3 (Recommendations for the authors):
(1) On line 431, "Cxxc1-deficient cells" should be Cxxc1-deficient Treg cells".
We thank the reviewer for highlighting this oversight. On line 431, we have revised "Cxxc1-deficient cells" to "Cxxc1-deficient Treg cells" to provide a more accurate and specific description. We appreciate the reviewer's attention to detail, as this correction improves the precision of our manuscript.
(2) In Figure 4H, negative values should be removed from the y-axis.
Thank you for your observation. We have revised Figure 4H to remove the negative values from the y-axis, as requested. This adjustment ensures a more accurate and meaningful representation of the data.
(3) It is better to provide the lists of overlapping genes in Figure 7C.
Thank you for your suggestion. We agree that providing the lists of overlapping genes in Figure 7C would enhance the clarity and reproducibility of the results. We have now included the gene lists as supplementary information (Supplementary Table 3) accompanying Figure 7C.
(1) Lee, J. H. & Skalnik, D. G. CpG-binding protein (CXXC finger protein 1) is a component of the mammalian set1 histone H3-Lys4 methyltransferase complex, the analogue of the yeast Set1/COMPASS complex. Journal of Biological Chemistry 280, 41725-41731, doi:10.1074/jbc.M508312200 (2005).
(2) Thomson, J. P., Skene, P. J., Selfridge, J., Clouaire, T., Guy, J., Webb, S., Kerr, A. R. W., Deaton, A., Andrews, R., James, K. D., Turner, D. J., Illingworth, R. & Bird, A. CpG islands influence chromatin structure via the CpG-binding protein Cfp1. Nature 464, 1082-U1162, doi:10.1038/nature08924 (2010).
(3) Shilatifard, A. in Annual Review of Biochemistry, Vol 81 Vol. 81 Annual Review of Biochemistry (ed R. D. Kornberg) 65-95 (2012).
(4) Brown, D. A., Di Cerbo, V., Feldmann, A., Ahn, J., Ito, S., Blackledge, N. P., Nakayama, M., McClellan, M., Dimitrova, E., Turberfield, A. H., Long, H. K., King, H. W., Kriaucionis, S., Schermelleh, L., Kutateladze, T. G., Koseki, H. & Klose, R. J. The SET1 Complex Selects Actively Transcribed Target Genes via Multivalent Interaction with CpG Island Chromatin. Cell Reports 20, 2313-2327, doi:10.1016/j.celrep.2017.08.030 (2017).
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Author response:
The following is the authors’ response to the original reviews.
Responses to Reviewer’s Comments:
To Reviewer #2:
(1) The use of two m<sup>5</sup>C reader proteins is likely a reason for the high number of edits introduced by the DRAM-Seq method. Both ALYREF and YBX1 are ubiquitous proteins with multiple roles in RNA metabolism including splicing and mRNA export. It is reasonable to assume that both ALYREF and YBX1 bind to many mRNAs that do not contain m<sup>5</sup>C.
To substantiate the author's claim that ALYREF or YBX1 binds m<sup>5</sup>C-modified RNAs to an extent that would allow distinguishing its binding to non-modified RNAs from binding to m<sup>5</sup>Cmodified RNAs, it would be recommended to provide data on the affinity of these, supposedly proven, m<sup>5</sup>C readers to non-modified versus m<sup>5</sup>C-modified RNAs. To do so, this reviewer suggests performing experiments as described in Slama et al., 2020 (doi: 10.1016/j.ymeth.2018.10.020). However, using dot blots like in so many published studies to show modification of a specific antibody or protein binding, is insufficient as an argument because no antibody, nor protein, encounters nanograms to micrograms of a specific RNA identity in a cell. This issue remains a major caveat in all studies using so-called RNA modification reader proteins as bait for detecting RNA modifications in epitranscriptomics research. It becomes a pertinent problem if used as a platform for base editing similar to the work presented in this manuscript.
The authors have tried to address the point made by this reviewer. However, rather than performing an experiment with recombinant ALYREF-fusions and m<sup>5</sup>C-modified to unmodified RNA oligos for testing the enrichment factor of ALYREF in vitro, the authors resorted to citing two manuscripts. One manuscript is cited by everybody when it comes to ALYREF as m<sup>5</sup>C reader, however none of the experiments have been repeated by another laboratory. The other manuscript is reporting on YBX1 binding to m<sup>5</sup>C-containing RNA and mentions PARCLiP experiments with ALYREF, the details of which are nowhere to be found in doi: 10.1038/s41556-019-0361-y.
Furthermore, the authors have added RNA pull-down assays that should substitute for the requested experiments. Interestingly, Figure S1E shows that ALYREF binds equally well to unmodified and m<sup>5</sup>C-modified RNA oligos, which contradicts doi:10.1038/cr.2017.55, and supports the conclusion that wild-type ALYREF is not specific m<sup>5</sup>C binder. The necessity of including always an overexpression of ALYREF-mut in parallel DRAM experiments, makes the developed method better controlled but not easy to handle (expression differences of the plasmid-driven proteins etc.)
Thank you for pointing this out. First, we would like to correct our previous response: the binding ability of ALYREF to m<sup>5</sup>C-modified RNA was initially reported in doi: 10.1038/cr.2017.55, (and not in doi: 10.1038/s41556-019-0361-y), where it was observed through PAR-CLIP analysis that the K171 mutation weakens its binding affinity to m<sup>5</sup>C -modified RNA.
Our previous experimental approach was not optimal: the protein concentration in the INPUT group was too high, leading to overexposure in the experimental group. Additionally, we did not conduct a quantitative analysis of the results at that time. In response to your suggestion, we performed RNA pull-down experiments with YBX1 and ALYREF, rather than with the pan-DRAM protein, to better validate and reproduce the previously reported findings. Our quantitative analysis revealed that both ALYREF and YBX1 exhibit a stronger affinity for m<sup>5</sup>C -modified RNAs. Furthermore, mutating the key amino acids involved in m<sup>5</sup>C recognition significantly reduced the binding affinity of both readers. These results align with previous studies (doi: 10.1038/cr.2017.55 and doi: 10.1038/s41556-019-0361-y), confirming that ALYREF and YBX1 are specific readers of m<sup>5</sup>C -modified RNAs. However, our detection system has certain limitations. Despite mutating the critical amino acids, both readers retained a weak binding affinity for m<sup>5</sup>C, suggesting that while the mutation helps reduce false positives, it is still challenging to precisely map the distribution of m<sup>5</sup>C modifications. To address this, we plan to further investigate the protein structure and function to obtain a more accurate m<sup>5</sup>C sequencing of the transcriptome in future studies. Accordingly, we have updated our results and conclusions in lines 294-299 and discuss these limitations in lines 109114.
In addition, while the m<sup>5</sup>C assay can be performed using only the DRAM system alone, comparing it with the DRAM<sup>mut</sup> control enhances the accuracy of m<sup>5</sup>C region detection. To minimize the variations in transfection efficiency across experimental groups, it is recommended to use the same batch of transfections. This approach not only ensures more consistent results but also improve the standardization of the DRAM assay, as discussed in the section added on line 308-312.
(2) Using sodium arsenite treatment of cells as a means to change the m<sup>5</sup>C status of transcripts through the downregulation of the two major m<sup>5</sup>C writer proteins NSUN2 and NSUN6 is problematic and the conclusions from these experiments are not warranted. Sodium arsenite is a chemical that poisons every protein containing thiol groups. Not only do NSUN proteins contain cysteines but also the base editor fusion proteins. Arsenite will inactivate these proteins, hence the editing frequency will drop, as observed in the experiments shown in Figure 5, which the authors explain with fewer m<sup>5</sup>C sites to be detected by the fusion proteins.
The authors have not addressed the point made by this reviewer. Instead the authors state that they have not addressed that possibility. They claim that they have revised the results section, but this reviewer can only see the point raised in the conclusions. An experiment would have been to purify base editors via the HA tag and then perform some kind of binding/editing assay in vitro before and after arsenite treatment of cells.
We appreciate the reviewer’s insightful comment. We fully agree with the concern raised. In the original manuscript, our intention was to use sodium arsenite treatment to downregulate NSUN mediated m<sup>5</sup>C levels and subsequently decrease DRAM editing efficiency, with the aim of monitoring m<sup>5</sup>C dynamics through the DRAM system. However, as the reviewer pointed out, sodium arsenite may inactivate both NSUN proteins and the base editor fusion proteins, and any such inactivation would likely result in a reduced DRAM editing.
This confounds the interpretation of our experimental data.
As demonstrated in Author response image 1A, western blot analysis confirmed that sodium arsenite indeed decreased the expression of fusion proteins. In addition, we attempted in vitro fusion protein purificationusing multiple fusion tags (HIS, GST, HA, MBP) for DRAM fusion protein expression, but unfortunately, we were unable to obtain purified proteins. However, using the Promega TNT T7 Rapid Coupled In Vitro Transcription/Translation Kit, we successfully purified the DRAM protein (Author response image 1B). Despite this success, subsequent in vitro deamination experiments did not yield the expected mutation results (Author response image 1C), indicating that further optimization is required. This issue is further discussed in line 314-315.
Taken together, the above evidence supports that the experiment of sodium arsenite treatment was confusing and we determined to remove the corresponding results from the main text of the revised manuscript.
Author response image 1.
(3) The authors should move high-confidence editing site data contained in Supplementary Tables 2 and 3 into one of the main Figures to substantiate what is discussed in Figure 4A. However, the data needs to be visualized in another way then excel format. Furthermore, Supplementary Table 2 does not contain a description of the columns, while Supplementary Table 3 contains a single row with letters and numbers.
The authors have not addressed the point made by this reviewer. Figure 3F shows the screening process for DRAM-seq assays and principles for screening highconfidence genes rather than the data contained in Supplementary Tables 2 and 3 of the former version of this manuscript.
Thank you for your valuable suggestion. We have visualized the data from Supplementary Tables 2 and 3 in Figure 4A as a circlize diagram (described in lines 213-216), illustrating the distribution of mutation sites detected by the DRAM system across each chromosome. Additionally, to improve the presentation and clarity of the data, we have revised Supplementary Tables 2 and 3 by adding column descriptions, merging the DRAM-ABE and DRAM-CBE sites, and including overlapping m<sup>5</sup>C genes from previous datasets.
Responses to Reviewer’s Comments:
To Reviewer #3:
The authors have again tried to address the former concern by this reviewer who questioned the specificity of both m<sup>5</sup>C reader proteins towards modified RNA rather than unmodified RNA. The authors chose to do RNA pull down experiments which serve as a proxy for proving the specificity of ALYREF and YBX1 for m<sup>5</sup>C modified RNAs. Even though this reviewer asked for determining the enrichment factor of the reader-base editor fusion proteins (as wildtype or mutant for the identified m<sup>5</sup>C specificity motif) when presented with m<sup>5</sup>C-modified RNAs, the authors chose to use both reader proteins alone (without the fusion to an editor) as wildtype and as respective m<sup>5</sup>C-binding mutant in RNA in vitro pull-down experiments along with unmodified and m<sup>5</sup>C-modified RNA oligomers as binding substrates. The quantification of these pull-down experiments (n=2) have now been added, and are revealing that (according to SFigure 1 E and G) YBX1 enriches an RNA containing a single m<sup>5</sup>C by a factor of 1.3 over its unmodified counterpart, while ALYREF enriches by a factor of 4x. This is an acceptable approach for educated readers to question the specificity of the reader proteins, even though the quantification should be performed differently (see below).
Given that there is no specific sequence motif embedding those cytosines identified in the vicinity of the DRAM-edits (Figure 3J and K), even though it has been accepted by now that most of the m<sup>5</sup>C sites in mRNA are mediated by NSUN2 and NSUN6 proteins, which target tRNA like substrate structures with a particular sequence enrichment, one can conclude that DRAM-Seq is uncovering a huge number of false positives. This must be so not only because of the RNA bisulfite seq data that have been extensively studied by others, but also by the following calculations: Given that the m<sup>5</sup>C/C ratio in human mRNA is 0.02-0.09% (measured by mass spec) and assuming that 1/4 of the nucleotides in an average mRNA are cytosines, an mRNA of 1.000 nucleotides would contain 250 Cs. 0.02- 0.09% m<sup>5</sup>C/C would then translate into 0.05-0.225 methylated cytosines per 250 Cs in a 1000 nt mRNA. YBX1 would bind every C in such an mRNA since there is no m<sup>5</sup>C to be expected, which it could bind with 1.3 higher affinity. Even if the mRNAs would be 10.000 nt long, YBX1 would bind to half a methylated cytosine or 2.25 methylated cytosines with 1.3x higher affinity than to all the remaining cytosines (2499.5 to 2497.75 of 2.500 cytosines in 10.000 nt, respectively). These numbers indicate a 4999x to 1110x excess of cytosine over m<sup>5</sup>C in any substrate RNA, which the "reader" can bind as shown in the RNA pull-downs on unmodified RNAs. This reviewer spares the reader of this review the calculations for ALYREF specificity, which is slightly higher than YBX1. Hence, it is up to the capable reader of these calculations to follow the claim that this minor affinity difference allows the unambiguous detection of the few m<sup>5</sup>C sites in mRNA be it in the endogenous scenario of a cell or as fusion-protein with a base editor attached?
We sincerely appreciate the reviewer’s rigorous analysis. We would like to clarify that in our RNA pulldown assays, we indeed utilized the full DRAM system (reader protein fused to the base editor) to reflect the specificity of m<sup>5</sup>C recognition. As previously suggested by the reviewer, to independently validate the m<sup>5</sup>C-binding specificity of ALYREF and YBX1, we performed separate pulldown experiments with wild-type and mutant reader proteins (without the base editor fusion) using both unmodified and m<sup>5</sup>C-modified RNA substrates. This approach aligns with established methodologies in the field (doi:10.1038/cr.2017.55 and doi: 10.1038/s41556-019-0361-y). We have revised the Methods section (line 230) to explicitly describe this experimental design.
Although the m<sup>5</sup>C/C ratios in LC/MS-assayed mRNA are relatively low (ranging from 0.02% to 0.09%), as noted by the reviewer, both our data and previous studies have demonstrated that ALYREF and YBX1 preferentially bind to m<sup>5</sup>C-modified RNAs over unmodified RNAs, exhibiting 4-fold and 1.3-fold enrichment, respectively (Supplementary Figure 1E–1G). Importantly, this specificity is further enhanced in the DRAM system through two key mechanisms: first, the fusion of reader proteins to the deaminase restricts editing to regions near m<sup>5</sup>C sites, thereby minimizing off-target effects; second, background editing observed in reader-mutant or deaminase controls (e.g., DRAM<sup>mut</sup>-CBE in Figure 2D) is systematically corrected for during data analysis.
We agree that the theoretical challenge posed by the vast excess of unmodified cytosines. However, our approach includes stringent controls to alleviate this issue. Specifically, sites identified in NSUN2/NSUN6 knockout cells or reader-mutant controls are excluded (Figure 3F), which significantly reduces the number of false-positive detections. Additionally, we have observed deamination changes near high-confidence m<sup>5</sup>C methylation sites detected by RNA bisulfite sequencing, both in first-generation and high-throughput sequencing data. This observation further substantiates the validity of DRAM-Seq in accurately identifying m<sup>5</sup>C sites.
We fully acknowledge that residual false positives may persist due to the inherent limitations of reader protein specificity, as discussed in line 299-301 of our manuscript. To address this, we plan to optimize reader domains with enhanced m<sup>5</sup>C binding (e.g., through structure-guided engineering), which is also previously implemented in the discussion of the manuscript.
The reviewer supports the attempt to visualize the data. However, the usefulness of this Figure addition as a readable presentation of the data included in the supplement is up to debate.
Thank you for your kind suggestion. We understand the reviewer's concern regarding data visualization. However, due to the large volume of DRAM-seq data, it is challenging to present each mutation site and its characteristics clearly in a single figure. Therefore, we chose to categorize the data by chromosome, which not only allows for a more organized presentation of the DRAM-seq data but also facilitates comparison with other database entries. Additionally, we have updated Supplementary Tables 2 and 3 to provide comprehensive information on the mutation sites. We hope that both the reviewer and editors will understand this approach. We will, of course, continue to carefully consider the reviewer's suggestions and explore better ways to present these results in the future.
(3) A set of private Recommendations for the Authors that outline how you think the science and its presentation could be strengthened
NEW COMMENTS to TEXT:
Abstract:
"5-Methylcytosine (m<sup>5</sup>C) is one of the major post-transcriptional modifications in mRNA and is highly involved in the pathogenesis of various diseases."
In light of the increasing use of AI-based writing, and the proof that neither DeepSeek nor ChatGPT write truthfully statements if they collect metadata from scientific abstracts, this sentence is utterly misleading.
m<sup>5</sup>C is not one of the major post-transcriptional modifications in mRNA as it is only present with a m<sup>5</sup>C/C ratio of 0.02- 0.09% as measured by mass-spec. Also, if m<sup>5</sup>C is involved in the pathogenesis of various diseases, it is not through mRNA but tRNA. No single published work has shown that a single m<sup>5</sup>C on an mRNA has anything to do with disease. Every conclusion that is perpetuated by copying the false statements given in the many reviews on the subject is based on knock-out phenotypes of the involved writer proteins. This reviewer wishes that the authors would abstain from the common practice that is currently flooding any scientific field through relentless repetitions in the increasing volume of literature which perpetuate alternative facts.
We sincerely appreciate the reviewer’s insightful comments. While we acknowledge that m<sup>5</sup>C is not the most abundant post-transcriptional modification in mRNA, we believe that research into m<sup>5</sup>C modification holds considerable value. Numerous studies have highlighted its role in regulating gene expression and its potential contribution to disease progression. For example, recent publications have demonstrated that m<sup>5</sup>C modifications in mRNA can influence cancer progression, lipid metabolism, and other pathological processes (e.g., PMID: 37845385; 39013911; 39924557; 38042059; 37870216).
We fully agree with the reviewer on the importance of maintaining scientific rigor in academic writing. While m<sup>5</sup>C is not the most abundant RNA modification, we cannot simply draw a conclusion that the level of modification should be the sole criterion for assessing its biological significance. However, to avoid potential confusion, we have removed the word “major”.
COMMENTS ON FIGURE PRESENTATION:
Figure 2D:
The main text states: "DRAM-CBE induced C to U editing in the vicinity of the m<sup>5</sup>C site in AP5Z1 mRNA, with 13.6% C-to-U editing, while this effect was significantly reduced with APOBEC1 or DRAM<sup>mut</sup>-CBE (Fig.2D)." The Figure does not fit this statement. The seq trace shows a U signal of about 1/3 of that of C (about 30%), while the quantification shows 20+ percent
Thank you for your kind suggestion. Upon visual evaluation, the sequencing trace in the figure appears to suggest a mutation rate closer to 30% rather than 22%. However, relying solely on the visual interpretation of sequencing peaks is not a rigorous approach. The trace on the left represents the visualization of Sanger sequencing results using SnapGene, while the quantification on the right is derived from EditR 1.0.10 software analysis of three independent biological replicates. The C-to-U mutation rates calculated were 22.91667%, 23.23232%, and 21.05263%, respectively. To further validate this, we have included the original EditR analysis of the Sanger sequencing results for the DRAM-CBE group used in the left panel of Figure 2D (see Author response image 2). This analysis confirms an m<sup>5</sup>C fraction (%) of 22/(22+74) = 22.91667, and the sequencing trace aligns well with the mutation rate we reported in Figure 2D. In conclusion, the data and conclusions presented in Figure 2D are consistent and supported by the quantitative analysis.
Author response image 2.
Figure 4B: shows now different numbers in Venn-diagrams than in the same depiction, formerly Figure 4A
We sincerely thank the reviewer for pointing out this issue, and we apologize for not clearly indicating the changes in the previous version of the manuscript. In response to the initial round of reviewer comments, we implemented a more stringent data filtering process (as described in Figure 3F and method section) : "For high-confidence filtering, we further adjusted the parameters of Find_edit_site.pl to include an edit ratio of 10%–60%, a requirement that the edit ratio in control samples be at least 2-fold higher than in NSUN2 or NSUN6knockout samples, and at least 4 editing events at a given site." As a result, we made minor adjustments to the Venn diagram data in Figure 4A, reducing the total number of DRAM-edited mRNAs from 11,977 to 10,835. These changes were consistently applied throughout the manuscript, and the modifications have been highlighted for clarity. Importantly, these adjustments do not affect any of the conclusions presented in the manuscript.
Figure 4B and D: while the overlap of the DRAM-Seq data with RNA bisulfite data might be 80% or 92%, it is obvious that the remaining data DRAM seq suggests a detection of additional sites of around 97% or 81.83%. It would be advised to mention this large number of additional sites as potential false positives, unless these data were normalized to the sites that can be allocated to NSUN2 and NSUN6 activity (NSUN mutant data sets could be substracted).
Thank you for pointing this out. The Venn diagrams presented in Figure 4B and D already reflect the exclusion of potential false-positive sites identified in methyltransferasedeficient datasets, as described in our experimental filtering process, and they represent the remaining sites after this stringent filtering. However, we acknowledge that YBX1 and ALYREF, while preferentially binding to m<sup>5</sup>C-modified RNA, also exhibit some affinity for unmodified RNA. Although we employed rigorous controls, including DRAM<sup>mut</sup> and deaminase groups, to minimize false positives, the possibility of residual false positives cannot be entirely ruled out. Addressing this limitation would require even more stringent filtering methods, as discussed in lines 299–301 of the manuscript. We are committed to further optimizing the DRAM system to enhance the accuracy of transcriptome-wide m<sup>5</sup>C analysis in future studies.
SFigure 1: It is clear that the wild type version of both reader proteins are robustly binding to RNA that does not contain m<sup>5</sup>C. As for the calculations of x-fold affinity loss of RNA binding using both ALYREF -mut or YBX1 -mut, this reviewer asks the authors to determine how much less the mutated versions of the proteins bind to a m<sup>5</sup>C-modified RNAs. Hence, a comparison of YBX1 versus YBX1 -mut (ALYREF versus ALYREF -mut) on the same substrate RNA with the same m<sup>5</sup>C-modified position would allow determining the contribution of the so-called modification binding pocket in the respective proteins to their RNA binding. The way the authors chose to show the data presently is misleading because what is compared is the binding of either the wild type or the mutant protein to different RNAs.
We appreciate the reviewer’s valuable feedback and apologize for any confusion caused by the presentation of our data. We would like to clarify the rationale behind our approach. The decision to present the wild-type and mutant reader proteins in separate panels, rather than together, was made in response to comments from Reviewer 2. Below, we provide a detailed explanation of our experimental design and its justification.
First, we confirmed that YBX1 and ALYREF exhibit stronger binding affinity to m<sup>5</sup>Cmodified RNA compared to unmodified RNA, establishing their role as m<sup>5</sup>C reader proteins. Next, to validate the functional significance of the DRAM<sup>mut</sup> group, we demonstrated that mutating key amino acids in the m<sup>5</sup>C-binding pocket significantly reduces the binding affinity of YBX1<sup>mut</sup> and ALYREF<sup>mut</sup> to m<sup>5</sup>C-modified RNA. This confirms that the DRAM<sup>mut</sup> group effectively minimizes false-positive results by disrupting specific m<sup>5</sup>C interactions.
Crucially, in our pull-down experiments, both the wild-type and mutant proteins (YBX1/YBX1<sup>mut</sup> and ALYREF/ALYREF<sup>mut</sup>) were incubated with the same RNA sequences. To avoid any ambiguity, we have included the specific RNA sequence information in the Methods section (lines 463–468). This ensures a assessment of the reduced binding affinity of the mutant versions relative to the wild-type proteins, even though they are presented in separate panels.
We hope this explanation clarifies our approach and demonstrates the robustness of our findings. We sincerely appreciate the reviewer’s understanding and hope this addresses their concerns.
SFigure 2C: first two panels are duplicates of the same image.
Thank you for pointing this out. We sincerely apologize for incorrectly duplicating the images. We have now updated Supplementary Figure 2C with the correct panels and have provided the original flow cytometry data for the first two images. It is important to note that, as demonstrated by the original data analysis, the EGFP-positive quantification values (59.78% and 59.74%) remain accurate. Therefore, this correction does not affect the conclusions of our study. Thank you again for bringing this to our attention.
Author response image 3.
SFigure 4B: how would the PCR product for NSUN6 be indicative of a mutation? The used primers seem to amplify the wildtype sequence.
Thank you for your kind suggestion. In our NSUN6<sup>-/-</sup> cell line, the NSUN6 gene is only missing a single base pair (1bp) compared to the wildtype, which results in frame shift mutation and reduction in NSUN6 protein expression. We fully agree with the reviewer that the current PCR gel electrophoresis does not provide a clear distinction of this 1bp mutation. To better illustrate our experimental design, we have included a schematic representation of the knockout sequence in SFigure 4B. Additionally, we have provided the original sequencing data, and the corresponding details have been added to lines 151-153 of the manuscript for further clarification.
Author response image 4.
SFigure 4C: the Figure legend is insufficient to understand the subfigure.
Thank you for your valuable suggestion. To improve clarity, we have revised the figure legend for SFigure 4C, as well as the corresponding text in lines 178-179. We have additionally updated the title of SFigure 4 for better clarity. The updated SFigure 4C now demonstrates that the DRAM-edited mRNAs exhibit a high degree of overlap across the three biological replicates.
SFigure 4D: the Figure legend is insufficient to understand the subfigure.
Thank you for your kind suggestion. We have revised the figure legend to provide a clearer explanation of the subfigure. Specifically, this figure illustrates the motif analysis derived from sequences spanning 10 nucleotides upstream and downstream of DRAMedited sites mediated by loci associated with NSUN2 or NSUN6. To enhance clarity, we have also rephrased the relevant results section (lines 169-175) and the corresponding discussion (lines 304-307).
SFigure 7: There is something off with all 6 panels. This reviewer can find data points in each panel that do not show up on the other two panels even though this is a pairwise comparison of three data sets (file was sent to the Editor) Available at https://elife-rp.msubmit.net/elife-rp_files/2025/01/22/00130809/02/130809_2_attach_27_15153.pdf
Response: We thank the reviewer for pointing this out. We would like to clarify the methodology behind this analysis. In this study, we conducted pairwise comparisons of the number of DRAM-edited sites per gene across three biological replicates of DRAM-ABE or DRAM-CBE, visualized as scatterplots. Each data point in the plots corresponds to a gene, and while the same gene is represented in all three panels, its position may vary vertically or horizontally across the panels. This variation arises because the number of mutation sites typically differs between replicates, making it unlikely for a data point to occupy the exact same position in all panels. A similar analytical approach has been used in previous studies on m6A (PMID: 31548708). To address the reviewer’s concern, we have annotated the corresponding positions of the questioned data points with arrows in Author response image 5.
Author response image 5.
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Here are 6 trims of the 2025 Mazda CX-90, what you get with each one, and the corresponding price tag
Here are the six Mazda CX-90 trim levels for 2025, including what you get with each one and the corresponding price tag
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2025 Mazda CX-30 S: The CX-30 S is the base model and, as a result, is the most affordable. It receives a full LED lighting setup, 16-inch alloy wheels, push-button start, and remote keyless entry. With its vast array of features and technology, the CX-30 S trim comes with a price tag of $26,415. 2025 Mazda CX-30 Select Sport: The Select Sport trim upgrades its base-level predecessor's limited features with a more polished entry system, a larger wheel setup of 18 inches, and turn signals integrated within its heated side mirrors. Additionally, rain-sensing wipers come as standard equipment combined with a leather-wrapped steering wheel, rear privacy glass, gear selector, and more. It has a price of $28,070. 2025 Mazda CX-30 Preferred: The Preferred trim includes a power moonroof, functional outside mirrors, as well as heated front seats coupled with the driver’s 8-way power (with lumbar and memory). As a result of these upgrades, the Preferred trim comes with a price of $30,360. 2025 Mazda CX-30 Carbon Edition: Moving up the 2025 Mazda CX-30 trim lineup, we find the Carbon Edition. This model offers the exclusive gray coloration with bold, black mirrors and wheels. Also, red leather enhances the cabin with HD radio (with 2 additional speakers), wireless smartphone charging, and more. These upgrades increase the MSRP for the Carbon Edition to $31,360. 2025 Mazda CX-30 Carbon Turbo: The Carbon Turbo trim is available exclusively in gold paint. However, that’s just the beginning of its differentiation. It also separates itself with beautiful terracotta leatherette-trimmed seats, a more pronounced 10.25-inch infotainment touchscreen, and a bold grille that matches its door mirrors. As a result, these upgrades push the Carbon Turbo’s MSRP to $34,360. 2025 Mazda CX-30 Premium: As we climb higher up the CX-30 hierarchy, we land on the Premium trim. True to form, this model lives up to its namesake by boasting signature LED headlights and a power liftgate. Also, navigation is standard, and the trim is equipped with a head-up display that uses traffic sign recognition. Moreover, a 12-speaker Bose sound system brings your satellite radio to life to create a well-connected and entertaining driving experience. The 2025 CX-30 Premium trim costs $33,560. 2025 Mazda CX-30 Premium Plus: The 2025 CX-30's top-of-the-line trim is the Premium Plus model. It boasts all the upscale features and specifications in addition to a 360-degree camera system, reverse emergency braking assistance connectivity, auto-dimming rearview mirror, and more. With all that it has to offer, the Premium Plus trim is priced at $38,370.
For each list item, take the vehicle model name (e.g. "2025 Mazda CX-30 S" and make it an H3, then put the associated paragraph content below it.
Headings and paragraph content shouldn't be formatted as a list and colons can be removed from the headings
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2025 Mazda CX-30 Trim Levels The 2025 Mazda CX-30 has 7 trim levels, each with a different set of features and attributes. Let’s explore each of these models in detail to determine which is the best for you. 2025 Mazda CX-30 S: The CX-30 S is the base model and, as a result, is the most affordable. It receives a full LED lighting setup, 16-inch alloy wheels, push-button start, and remote keyless entry. With its vast array of features and technology, the CX-30 S trim comes with a price tag of $26,415. 2025 Mazda CX-30 Select Sport: The Select Sport trim upgrades its base-level predecessor's limited features with a more polished entry system, a larger wheel setup of 18 inches, and turn signals integrated within its heated side mirrors. Additionally, rain-sensing wipers come as standard equipment combined with a leather-wrapped steering wheel, rear privacy glass, gear selector, and more. It has a price of $28,070. 2025 Mazda CX-30 Preferred: The Preferred trim includes a power moonroof, functional outside mirrors, as well as heated front seats coupled with the driver’s 8-way power (with lumbar and memory). As a result of these upgrades, the Preferred trim comes with a price of $30,360. 2025 Mazda CX-30 Carbon Edition: Moving up the 2025 Mazda CX-30 trim lineup, we find the Carbon Edition. This model offers the exclusive gray coloration with bold, black mirrors and wheels. Also, red leather enhances the cabin with HD radio (with 2 additional speakers), wireless smartphone charging, and more. These upgrades increase the MSRP for the Carbon Edition to $31,360. 2025 Mazda CX-30 Carbon Turbo: The Carbon Turbo trim is available exclusively in gold paint. However, that’s just the beginning of its differentiation. It also separates itself with beautiful terracotta leatherette-trimmed seats, a more pronounced 10.25-inch infotainment touchscreen, and a bold grille that matches its door mirrors. As a result, these upgrades push the Carbon Turbo’s MSRP to $34,360. 2025 Mazda CX-30 Premium: As we climb higher up the CX-30 hierarchy, we land on the Premium trim. True to form, this model lives up to its namesake by boasting signature LED headlights and a power liftgate. Also, navigation is standard, and the trim is equipped with a head-up display that uses traffic sign recognition. Moreover, a 12-speaker Bose sound system brings your satellite radio to life to create a well-connected and entertaining driving experience. The 2025 CX-30 Premium trim costs $33,560. 2025 Mazda CX-30 Premium Plus: The 2025 CX-30's top-of-the-line trim is the Premium Plus model. It boasts all the upscale features and specifications in addition to a 360-degree camera system, reverse emergency braking assistance connectivity, auto-dimming rearview mirror, and more. With all that it has to offer, the Premium Plus trim is priced at $38,370.
Move this section below the sentence ending with "and boasts a selection of both non-turbo as well as turbocharged gas engine options."
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Reply to the reviewers
Reviewer #1:
Major Comments:
- The data in the paper strongly suggests that the new copper shuttles are selective for copper and have faster binding kinetics (Fig 1) than the previous one. However, the data regarding the copper shuttling from the copper(Aβ) peptides is not very convincing. It appears to be due to the Cu effect alone (Fig.3), as the reduction in viability with Cu(II)+ AscH- is almost the same as the Cu(II)(Aβ)+AscH-. To convincingly show that the peptide shuttle can strip copper from (Aβ) peptides, the authors need to show that the copper is bound to the (Aβ) peptide before it is used in the experiment. Rightfully so, the effect of the toxicity of Cu(II)+ AscH- is similar to that of Cu(II)(Aβ16)+AscH-. This is due to the fact that Aβ16 is not toxic to the cells, so therefore there is no compounded effect of Cu and Aβ16 as seen for Cu(II)(Aβ40). As for the toxicity of Cu(II)+ AscH-, it is be similar to Cu(II)(Aβ)+AscH- because Cu(II) will be bound to a weaker ligand in the medium and such loosely bound Cu is also able to produce ROS with AscH- with similar rates as Cu-Ab.
Data from our lab and others have shown that in HEPES solution at pH 7.4, Aβ forms a complex with Cu. The present work is also in line with Cu-binding to Ab, as in Figure 1C (GSH), the rate of Cu withdrawal by the shuttle can only be explained by Cu bound to Ab, as Cu in the buffer binds to the shuttle much faster. Also, the AscH- consumption rate measured in Fig S5D-E are congruent of Cu bound to Ab, unbound Cu has a much faster rate of AscH- consumption (Santoro et al. 2018, doi.org/10.1039/C8CC06040A).
The concentrations of Aβ and Cu used in our experimental condition were determined with a UV-Vis spectrophotometer.
Minor comments:
- The paper does not cite Figure 1A and some supplementary figures, especially Supp. Fig. 1-2. All the figures and supplementary figures should be cited. This has been rectified for all the concerned figures.
The data presentation in Figures 3B and S8 is confusing."-" signs indicate no addition or the blank box means no addition. Also, the AKH-αR5W4 has no "-" sign in the first bar. For clarity, please indicate the -, +, or no sign means in the figure legends. Also, what does "Batch A" refer to in Figure 3B?
The figures have been modified as suggested by the reviewer.
Page 7, correct (Error! Referencesource not found.Figure 1C).
This has been rectified.
The Giantin staining in Figure 2B is making it hard to visualize ATP7A trafficking. If the Giantin image overlay is removed, it may be easier to see the movement of ATP7A from the perinuclear region to the vesicles.
The images have been modified to better appreciate the ATP7A change in distribution upon the increase in intracellular Cu level. We have reduced the number of conditions for which images are provided and provided individual staining for clarity. Zoomed images are also provided. The remainder of the conditions are in Figure S7B
In the introduction, the authors mention, "These molecules have, however, a major pitfall as is seen for Elesclemol, a candidate for Menkes disease treatments 32. The authors cite reference " Tsvetkov, P. et al. Copper induces cell death by targeting lipoylated TCA cycle proteins." The paper showing elesclomol as a candidate for Menkes disease treatments is Guthrie L et al., Elesclomol alleviates Menkes pathology and mortality by escorting Cu to cuproenzymes in mice. Science. 2020.
We thank the reviewer for pointing this out, which was apparently not clearly explained. Our intention here was to show that a major pitfall of shuttles like Elesclomol, as seen in the study by Tsvetkov, P. et al. Science (2022), is cuprotoxicity. The sentence has been clarified and the work of Guthrie L et al is cited for Elesclomol as a candidate for Menkes disease.
Reviewer #2 :
Major issues:
- This reviewer is not convinced that the authors' experimental system is well suited for studies of glia activation and protective effects. With the exception of a couple of panels it is very hard to see differences. The authors should significantly improve the quality of images in Figure 5 to make this set of data convincing. We thank the reviewer for his/her detailed evaluation and for bringing to light the quality of the image in Figure 5. We have therefore improved the quality of the images by improving the signal to noise ratio to better show the differences between conditions.
Similarly, the quality of giantin staining is low and needs to be improved and more experimental details are needed (see details below).
As stated in our answer to reviewer 1, the images have been modified to better appreciate ATP7A redistribution upon increase of intracellular Cu levels. We have reduced the number of conditions for which images are provided and provided individual staining for clarity. Zoomed images are also provided. The remainder of the conditions are in Figure S7B.
Given that shuttles are found within vesicles, the authors should discuss the mechanism through which Cu is released into the cytosol to trigger ATP7B trafficking.
The mechanism of Cu escape from endosomes remains poorly understood. However, supported by our recent observations that Cu quickly (within 10 min) dissociates from the Cu-shuttle AKH-αR5W4NBD in endosomes (Okafor et al., 2024, /doi.org/10.3389/fmolb.2024.1355963), we discuss the potential involvement CTR1/2 and DMT1 (page 16).
There are numerous small writing issues that make paper difficult to read. The authors are encouraged to carefully edit their manuscript.
We thank the reviewer for pointing this out and several errors have been corrected whereas various sentences have been clarified.
Minor issues
* „A solution of monomerized Aβ complex in 10% DMEM (diluted with DMEM salt solution) was prepared in microcentrifuge tubes" - here and further the description of media composition is confusing What is the rest 90%?
This has been rectified. The composition of the salt solution that makes up the 90% has been provided (page 4).
* „Afterwards, AscH- was added to the tubes and vortexed, the mixture was then added to PC12 cells" - concentration of ascorbate is mentioned only once (later in the figure legend) where it can be barely found, also without explaining the choice of concentration. Additionally, ascorbate's product code is not listed. Please, correct.
These points have been rectified.
* Description of the cell (PC12 line) handling conditions is absent (growth medium, passage number used etc) and should be included.
This information is now provided.
* ATP7A delocalization assay. Details for the secondary antibodies are absent (full name (e.g. AlexaFluor 488), manufacturer, code) and should be added.
Missing information has been added.
* page 6: „Next, we investigated the capacity of the shuttles to withdraw Cu(II) from cell culture media, DMEM 10% and DMEM/F12 1:1 (D/F)." Here and further explanation is needed why the mixture of DMEM/F12 is needed (F12 is also not listed in the materials list).
DMEM/F12 is a media that is commercially available used for some cell types, and it has been added to the materials list (page 4).
* Page 7. Legend to the figure 1B: „Conditions: Cu(II)=AKH-αR5W4NBD=DapHH-αR5W4NBD=HDapH-αR5W4NBD= 5 μM, DMEM 10%, D/F 100%, 25{degree sign}C, n=3." - „DMEM/F12" ratio equals to „100%" is confusing, please clarify
This has been clarified.
* Page 8-9. Legend to the Figure 2A. „Similar observations were obtained with 5 different cell cultures." Same remark goes to the legend to supplementary figure 7 ("Similar observations were obtained with at least 3 different cell cultures"). Do the authors mean independent experiments or different cell lines? Please clarify. If different cell lines, consider including these data into the supplement.
Indeed we meant independent experimentations. This has been clarified.
* Page 8-9, figure 2B. Giantin is a cis-golgi marker, which should localize perinuclearly. In the cells shown the signal is diffuse and appears non-specific. Please improve the quality.
We have reduced the number of conditions for which images are provides and are providing individual staining for clarity. Zoomed images are also provided allowing visualization of the typical cis-Golgi distribution of Giantin.
* Page 8-9, figure 2B. ATP7A is shown in green. The authors did not specify the secondary antibody has been used for it. If the secondary antibody used for labeling of ATP7A has green fluorescence then how does one distinguish between the transporter signal and signal of the green fluorescent shuttle? Please provide more details.
We thank the reviewer for pointing this point as we missed to mention this technical issue in the original manuscript. The Cu-shuttles labeled with NBD indeed emit in the green signal, but they are not fixable under our conditions and are washed out during ICC procedure. Accordingly, they do generate any background signal and do not interfere with the ICC as shown by the controls and test conditions (Figure S7B and Figure 2B). This is now mentioned (page 11).
* Page 9 and Figure 2B. Why did authors use Cu(II)EDTA for the experiment? What was the concentration? Please, add this information as well as Cu(II)GTSM treatment conditions to the experiment description in materials and methods.
EDTA is a strong chelator of Cu(II), however due to its negative charge it cannot penetrate the plasma membrane thus importing Cu. It is therefore used as a negative control, to eliminate the speculation of Cu non-specifically crossing the plasma membrane or through a channel.
* Figure 2 and supplementary figure 7. It would be beneficial to have higher magnification images. Please, add them, if possible.
These higher magnification images have been provided.
* Page 11. „In conclusion, the novel Cu(II)-selective peptide shuttles .... capable of instantly preventing ... toxicity on PC12 cells, whereas ... instantly rescue Cu(II)Aβ1-42 toxicity". Authors should be more careful with terminology. According to the materials and methods, the survival assay was carried out after 24h of cells' treatment with the reagents. Effect visible after 24h and „instant rescue" is not the same, Please clarify or modify the wording
In principle, the peptides cannot reverse the production of ROS, however they prevent ROS production. Therefore, for the peptides to have an effect, they have to instantly halt ROS production. This is justified by the novel shuttles being more effective than AKH-αR5W4NBD in preventing toxicity, given we modified just the Cu binding sequence. We have however restricted the use of the term instantly to ROS production.
* Page 13, figure 5, panels C and D. In both quantitations Cu(II) was used as one of the control conditions. Why in panel D the percentage of activated microglial cells (second graphs from right) is several fold higher (appr. 150% vs >500%)?
This variability was observed throughout our set of experiments and could be linked to the quality of the hippocampal slices used. Slight variations in the age of the animals or in the traces of metals in the mediums are likely explanations. However, the different groups that are compared represent experiments performed simultaneously.
* Supplementary Figure S3B. The lowest solid line does not correspond to any color in the legend (please, check and correct). However, by the method of exclusion, one may conclude that it refers to Cu(II)+HDapH-shuttle. What could be a potential explanation for stronger quenching of this shuttle by binding Cu(II) directly from the spiked media comparing to when it is pre-complexed with copper (also supported by the panel D)?
The stronger quenching of this shuttle by binding Cu(II) directly from the spiked media comparing to when it is pre-complexed with copper is not significant.
* In discussion the authors mention that the designed shuttles are prone to degradation in 48 hours. In the viability assays, they treat cells for 24 hours, in the fluorescent and confocal microscopy experiments for one hour or less. What is the lifetime of these shuttle peptides in the cells?
The lifetime of the shuttle peptide in the cells is currently unknown. However, after 24h incubation of PC12 cells with the AKH-αR5W4NBD, DapHH-αR5W4NBD and HDapH-αR5W4NBD, the Cu shuttles lose their punctate distribution and appear diffuse inside the cells. We have recently shown that AKH-αR5W4NBD cycles through different endosomal compartments and eventually reaches the lysosomes where it could be degraded (Okafor et al., 2024, /doi.org/10.3389/fmolb.2024.1355963). Therefore, the diffuse distribution of the fluorescence signal could suggest degradation of the Cu-shuttles.
* From the microscopy observations, the mechanism of entry of apo-shuttles (with no Cu(II) in the complex) and in complex with Cu(II) looks quite different. Namely, in figure S7 the fluorescent signal is very strong in the plasma membrane with significantly less vesicular pattern when compared to figure 2A. It is especially apparent for DapHH shuttle at 15 minutes of incubation. Can authors hypothesize/discuss the reason for these differences?
The difference of the shuttle’s signal in the presence or absence of Cu binding, is due to fluorescence quenching by Cu bound and was at the heart of the design of these shuttles. Hence a strong signal at the plasma membrane is seen in the absence of Cu as these CPP-based shuttles interact strongly with the plasma membrane. However in presence of Cu, they become less visible due to quenching by Cu. Interestingly however, is that when Cu dissociates from the shuttle inside the cells (likely in acid endosomes), this quenching is suppressed and the fluorescence reappears. This is now better explained (page 10).
* Please, show the figures in the supplementary file in the same order as you refer to them.
This has been rectified.
* Introduction. Description of the shuttle peptides: „(3) a cell penetrating peptide (CPP), αR5W4, with sequence RRWWRRRWWR, for cell entry35" - one R is the middle is extra.
This has been rectified.
*Kd units are missing (pages 2, 3 and 15) and should be added.
This has been added.
* Figure 1A is either not referred at all or mislabeled.
* Page 7, Figure 1B: x axis on the second panel (+Mn+) misses a label.
* Page 8. „Upon addition of DapHH-αR5W4NBD or HDapH-αR5W4NBD, an immediate slow-down in ROS production was observed (Figure 1D and S1E), ..." - mislabeled supplementary figure, please, correct.
* Page 11. „...but not in the presence of AKH-αR5W4NBD which required pre-incubation to prevent toxicity (Figure 3AFigure)." Please, correct the reference to the figure.
* Page 11. „This is in line with the faster retrieval ... previously demonstrated in vitro (Figure 1)" - please, specify the panel.
* Supplementary materials and methods, subsection „Retrieval of Cu by peptide shuttles from Aβ", page 2: „The same was done for 10 μM Cu(II)...to give the estimated 100% saturated emission level." - check the spelling of the shuttle species.
* Supplementary Figure S4. By the behavior of AKH-shuttle in the presence of copper and other metals, it looks that panels are shuffled, i.e. panel C looks corresponding to the panel B with DMEM/F12 conditions, whish is also supported by the values in the Table S1. Please, check and correct, if needed.
* Supplementary figure S9, panel A. Apparently, mislabeled images with Abeta1-42 and Cu(II)Abeta1-42. Please, correct.
We apologize for the different issues in referencing figures. This has been rectified.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
Minor Concerns
I think that authors can add some concepts of general interest on AD, as follows
evidence showed that AD top-line disease-modifying drugs employing monoclonal antibodies (donanemab, lecanemab, and aducanumab) that tag Aβ, based on the 'Amyloid cascade hypothesis', are able to rid the brain of Aβ plaques, but the drug benefits consist in a reduction of 35% of cognitive decline. The remaining disease burden (more than 65%) has no disease-modifying therapeutic options, at the moment. Furthermore, monoclonal antibodies against Aβ have strong side- events (ARIA). On this basis, it could be suggested that removing Aβ plaque might not be sufficient to slow the 100% percentage of clinical decline in AD. This is why the Cu(II) shuttle invention presented by the candidate may represent a valid and concrete means to fight AD, since also meta-analyses demonstrate that Cu and more specifically non-Cp Cu is increased in AD (PMID: 34219710). The authors can add some of these clinical considerations in the Discussion.
There is only a very brief description of the scenario of evidence of the involvement of copper in Alzheimer's, especially from a clinical point of view, I mean the scenario resulting from clinical studies carried out on AD patients. This would have highlighted the unmet medical need to which these new compounds (the Cu shuttles) can provide an answer. At least for a subpopulation of Alzheimer's patients, and we know that there are different subtypes of Alzheimer's disease (for example 10.1016/j.neurobiolaging.2004.04.001, but authors can find others), these Cu(II) selective shuttles could provide beneficial effects. Literature reports about a percentage of AD patients with increased levels of Cu (some papers on this topic e can be easily retrieved,), who may primarily benefit from these compounds. These can be easily identified as it is also characterized by a different biochemical, cognitive, and genetic profile. The current study is timely since AD patients with high Cu can be easily identified since they are characterized by a different biochemical, cognitive, and genetic profile as per recent findings (PMID: 37047347). This information can improve the quality of the manuscript by providing information about the unmet clinical need that this study can answer
We thank the reviewer for his very positive evaluation and for his suggestion that gives more perspective to our work. Accordingly, we have added these parts to the introduction and discussion sections.
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Referee #3
Evidence, reproducibility and clarity
Summary: The paper addresses the design and synthesis of novel copper (Cu)-selective peptide transporters to prevent Cu(Aβ)-induced toxicity and microglial activation in organotypic hippocampal slices.This is a very interesting study. I would define the study as pioneering and I hope that it is a seminal study, as it could be a study that opens the doors to future studies in the sector but above all applications in the clinical field. The methods are very complex and demonstrate an excellent knowledge of the biochemistry of beta-amyloid and copper. Methods are also clear and provide information for reproducibility
Minor Concerns
I think that authors can add some concepts of general interest on AD, as follows evidence showed that AD top-line disease-modifying drugs employing monoclonal antibodies (donanemab, lecanemab, and aducanumab) that tag Aβ, based on the 'Amyloid cascade hypothesis', are able to rid the brain of Aβ plaques, but the drug benefits consist in a reduction of 35% of cognitive decline. The remaining disease burden (more than 65%) has no disease-modifying therapeutic options, at the moment. Furthermore, monoclonal antibodies against Aβ have strong side- events (ARIA). On this basis, it could be suggested that removing Aβ plaque might not be sufficient to slow the 100% percentage of clinical decline in AD. This is why the Cu(II) shuttle invention presented by the candidate may represent a valid and concrete means to fight AD, since also meta-analyses demonstrate that Cu and more specifically non-Cp Cu is increased in AD (PMID: 34219710). The authors can add some of these clinical considerations in the Discussion
there is only a very brief description of the scenario of evidence of the involvement of copper in Alzheimer's, especially from a clinical point of view, I mean the scenario resulting from clinical studies carried out on AD patients. This would have highlighted the unmet medical need to which these new compounds (the Cu shuttles) can provide an answer. At least for a subpopulation of Alzheimer's patients, and we know that there are different subtypes of Alzheimer's disease (for example 10.1016/j.neurobiolaging.2004.04.001, but authors can find others), these Cu(II) selective shuttles could provide beneficial effects. Literature reports about a percentage of AD patients with increased levels of Cu (some papers on this topic e can be easily retrieved,), who may primarily benefit from these compounds. These can be easily identified as it is also characterized by a different biochemical, cognitive, and genetic profile. The current study is timely since AD patients with high Cu can be easily identified since they are characterized by a different biochemical, cognitive, and genetic profile as per recent findings (PMID: 37047347). This information can improve the quality of the manuscript by providing information about the unmet clinical need that this study can answer
Significance
The significance of the study relies on that the Cu(II) selective shuttles can import Cu into cells and also release Cu once inside the cells, which was shown to be bioavailable, as revealed by the delocalization of ATP7A from the TGN to the sub-plasmalemma zone in PC12 cells. The novelty is well expressed by the implementation of Cu(II) selective shuttles that can release Cu inside the cells. Thus, they can restore Cu physiological levels in conditions of brain Cu deficiency that typify the neuronal cells in AD. Furthermore, this Cu trafficking can be finely tuned, thus preventing potential adverse drug reactions when transferred into human clinical phase I and II studies. This application may represent a step forward concerning previous copper attenuating compounds/Cu(II) ionophores such as Clioquinol and GTSM which mediated non-physiological Cu import into the cells that have likely contributed to neurotoxicity processes in previous unsuccessful phase II clinical trials.
Furthermore, the originality of the current study relies on the fact that these shuttles can be tracked in real-time, once in the cell, since they employ a fluorophore moiety sensitive to Cu binding. Furthermore, DapHH-αR5W4NBD and HDapH-αR5W4NBD, can import bioavailable Cu(II) and can prevent ROS production by Cu(II)Aβ instantly, due to the much faster Cu-binding. Importantly, DapHH-αR5W4NBD and HDapH-αR5W4NBD shuttles have been also capable of preventing OHSC slices from Cu-induced neurotoxicity, microglial proliferation, and activation. Another important feature of the Cu shuttles is that they can be designed to control their site of cell delivery. In fact, previous ionophores had the tendency to accumulate in the mitochondria, and, in doing so, excess Cu in the mitochondria might have competed with other transitional metals (mainly Fe) and triggered mitochondrial dysfunction as well as cuproptosis. These are the main strengths of the study.
The audience of this article is currently that of expert biochemists, but by adding aspects regarding the unmet clinical need relating to the large population of AD patients with high copper in the introduction and discussion, the article can capture the attention of clinicians.
I am a neuroscientist working on biochemical pathways and metals in Alzheimer's disease.
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Reply to the reviewers
*Reviewer #1 (Evidence, reproducibility and clarity (Required)): *
- The authors investigate in this study the function of LIN-42 for the process of precise molting timing in C. elegans. To achieve this, they compare LIN-42 with its mammalian ortholog, Period. They found that similar to Period, LIN-42 interacted with the kinase KIN-20, a mammalian Casein kinase 1 (CK1) ortholog. Hence, two different proteins involved in rhythmic processes, LIN-42 and Period function in a conserved manner. *
- First, they used mutants with specific deletions to untangle various phenotypes during C. elegans development. From this analysis they identify a specific region, corresponding to a CK1-binding region in mammals, to be mainly involved in the rhythmic molting phenotype. Next, they identify KIN-20, the CK1 ortholog as interaction partner of LIN-42. They even were able to demonstrate an interaction of CK1 with the region of LIN-42. Using CK1, they identified potential phosphorylation sites within LIN-42 and compared those with immunoprecipitated protein in vivo. There was a substantial overlap. While the C-terminal tail of LIN-42 was heavily phosphorylated, deletion of the C-terminal part resulted only in a minor phenotype for rhythmic molting. Last but not least, they demonstrated that point mutations that inactivate the catalytic function of KIN-20 produced a rhythmic molting phenotype. The interaction of LIN-42 with KIN-20 affected the localization of the kinase, similar to what was found to Period and CK1. *
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Overall, the experiments are well done, well controlled and well described even for non-specialists. I guess it was not easy to kind of sort out the many overlapping phenotypes. It was certainly helpful just to focus on the clear rhythmic molting phenotype. *
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I have no major or minor comments. *
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Reviewer #1 (Significance (Required)): *
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The manuscript is well written and can be followed by non-specialists of the field. The experiments are well performed. Even if some experiments did not yield the expected phenotype, e.g. deletion of the C-terminal tail of LIN-42 had only a minor phenotype inspire of heavy phosphorylation, these experiments are anyhow included and explained. *
- Overall, the study is interesting for people in the C. elegans field and by similarity mammalian chronobiology. I would expect that most of the progress based on this study will be on the further elucidation of the molting phenotype and how the other phenotypes related to this. Then this could emerge as a blueprint for molting phenomena in other species as well. *
- I am a mammalian chronobiologist working on Period proteins. *
We thank the reviewer for their positive evaluation of our work.
*Reviewer #2 (Evidence, reproducibility and clarity (Required)): *
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This study represents pioneering work on LIN-42, the C. elegans ortholog of PER, uncovering its role in molting rhythms and heterochronic timing. A key strength of this work lies in its integrative approach, combining genetic and developmental analyses in C. elegans with biochemical characterization of LIN-42 protein. *
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At the organismal level, the authors take advantage of the power of C. elegans as a model system, employing precise genetic manipulations and high-resolution developmental assays to dissect the contributions of LIN-42 and its interaction partner KIN-20, the C. elegans ortholog of CK1, to molting rhythms. Their findings provide in vivo evidence that binding of LIN-42 with KIN-20 promotes the nuclear accumulation of KIN-20 and is crucial for molting rhythms, while its PAS domain appears dispensable for this function. This detailed phenotypic analysis of multiple LIN-42 and KIN-20 mutants represents a significant contribution to our understanding of the developmental clock. *
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At the biochemical level, the study provides a detailed analysis of the mechanism underlying LIN-42's interaction with CK1, demonstrating that LIN-42 contains a functionally conserved CK1-binding domain (CK1BD). Through their in vitro kinase assays and structural insights, the authors identified distinct roles for CK1BD-A and CK1BD-B: the former in kinase inhibition and the latter in stable CK1 binding and phosphorylation. Importantly, their data align well with previous findings on PER-CK1 regulation in mammalian and Drosophila systems, reinforcing the evolutionary conservation of key clock components. *
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Overall, this work stands out for its deep and important insights into how CK1-mediated regulation extends beyond the circadian clock to regulate the developmental clock. The combination of genetic approaches with biochemical analyses makes this an outstanding contribution to both chronobiology and nematode developmental biology. *
We thank the reviewer for the strong endorsement for publication of our work
*Major comment 1: * * In Figure 2D, I could not find a crucial control if the authors claim that KIN-20 binds to LIN-42. For example, a single mutant of LIN-42-3xFLAG could be used as a control for the double mutant. *
We will do an appropriate control experiment.
*Major comment 2: * * The sizes of the KIN20 bands were very diverged (~40 kDa and ~60 kDa), but the authors provide no explanation for this. *
The worm produces several KIN-20 isoforms. We will state this in the revised manuscript.
*Major comment 3: * * Regarding the MS study, the raw data are available, but the detailed supplemental Excel files would be more informative for readers. For example, are other interactors such as REV-ERB/NHR-85 detected in Figure 2A? Regarding Figure 4F, the list of phosphorylation sites and MS scores is also informative. *
We apologize for our omission in stating clearly in the figure legend that the significantly enriched proteins were labeled with a red dot. These were only LIN-42 itself and KIN-20. NHR-85 was not enriched. We will state this explicitly in a revised version and provide all relevant information.
*Major comment 4: * * It is an important finding that the PAS domain of LIN-42 is not essential for the molting rhythms. Is the PAS domain also dispensable for binding with KIN-20? *
Although we have currently no reason to assume that the PAS domain would be required for KIN-20 binding, we will perform an in vitro experiment to test for binding.
*Major comment 5 (Optional): * * In this study, the authors carefully performed in vitro kinase assays, and I strongly suggest that they investigate whether the CKI-mediated phosphorylation of LIN-42 is temperature-compensated and whether the CKI-BD-AB regions affect it. *
Although this is an interesting question, addressing it appears outside the scope of the manuscript and a revision; please see section 4 below.
*Major comment 6 (Optional): * * In Figure 6, the authors argue that the CKI-BD of LIN-42 is important for CK1 nuclear translocation. It would be better to show the effect of the nuclear accumulation of CKI on nuclear proteins, like the mammalian CKI-PER2-CLOCK story. Does CKI localization affect phosphorylation status of other clock-related proteins including REV-ERB/NHR-85? * * Phospho-proteome analysis would identify nuclear substrates of CK1. In addition, is phosphorylation of LIN-42 dispensable for the CK1 nuclear translocation? *
This is another interesting question yet currently nothing is known about other CK1/KIN-20 targets, and we have no evidence for NHR-85 being one. Please see our detailed comments in the section 4 below.
To address whether LIN-42 phosphorylation affects CK1/KIN-20 nuclear accumulation, we will seek to examine KIN-20 localization in LIN-42∆Tail animals.
*Major comment 7 (Optional): * * LIN-42 rhythmic expression could drive rhythmic nuclear accumulation of KIN-20. It would be better to examine this possibility using kin-20::GFP in lin-42 mutants. *
We agree that the mutant analysis is important for this and Fig. 6C shows reduced KIN-20 nuclear accumulation in LIN-42∆CK1BD.
Minor 1: * * I could not find the full gel images of the Western blot analyses as supplemental materials.
This data will be added.
Minor 2: * * The authors discussed a conserved module in two different clocks. A statement regarding a recently published paper (Hiroki and Yoshitane, Commun Biol, 2024) would be informative for readers.
We will add such a statement.
***Referee cross-commenting** *
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I basically agree with reviewer 1 and hope that this paper will be published soon as it is very valuable for our field. I have constructively pointed out some parts that could be improved, but depending on the editor's judgement, I believe that even if not all of these are revised, it will be sufficient for publication. *
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Reviewer #2 (Significance (Required)): *
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This work stands out for its deep and important insights into how CK1-mediated regulation extends beyond the circadian clock to regulate the developmental clock. The combination of genetic approaches with biochemical analyses makes this an outstanding contribution to both chronobiology and nematode developmental biology. *
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I strongly suggest editors to accept this study with minor modifications according to the following comments.*
We thank the reviewer for their strong support and the clear indication of required vs. optional revisions.
*Reviewer #3 (Evidence, reproducibility and clarity (Required)): *
- In their manuscript "A conserved chronobiological complex times C. elegans development", Spangler, Braun, Ashley et al. investigate the mechanisms through which the PERIOD orthologue, lin-42, regulates rhythmic molting in C. elegans. Through precise genetic manipulations, the authors identify a particular region of lin-42, the 'CK1BD', which regulates molting timing, with less effect on other lin-42 phenotypes (e.g. heterochrony). They show that LIN-42 and the casein kinase 1 (CK1) homologue KIN-20 interact in vivo, and identify phosphorylation sites of LIN-42. Using biochemical assays, they find that the CK1BD of LIN-42 is sufficient for interaction with the human homologue of KIN-20, CK1, in vitro. The LIN-42 CK1BD is also required for the proper nuclear accumulation of KIN-20 in vivo. Furthermore, a point mutation that should disrupt the catalytic activity of KIN-20 also shows an irregular molting phenotype, similar to the lin-42 CK1BD mutant. The manuscript is very well-written and the data and methods are well-presented and detailed. Overall this work makes a convincing case that the C. elegans lin-42:Kin-20 and mammalian period:Ck1 interactions have functionally conserved roles in the oscillatory developmental programs of each organism (molting timing and circadian rhythms, respectively), with a few caveats below that can be addressed.*
We thank the reviewer for their positive evaluation of our work.
*Major comments: *
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- The authors have shown that LIN-42 is phosphorylated in vivo, but the dependence of this phosphorylation on KIN-20 is not fully addressed. In the discussion (lines 417-420), the authors mention that the unhealthy phenotype of the kin-20 mutant animals prevented them from assessing LIN-42 phosphorylation in this genetic background. To bolster their model and to circumvent this issue, it should be feasible to generate a kin-20 degron allele and to perform the LIN-42 phospho-proteomics upon inducible degradation. Alternatively, perhaps a phos-tag western blot for LIN-42 could be used to compare the kin-20 wild-type to kin-20 mutants.*
We agree, and acknowledged in the discussion, that phoshorylation of LIN-42 by KIN-20 in vivo has not been demonstrated by us. However, as discussed in the section 4 below, we find that this costly, challenging and time-consuming experiment is not warranted by the expected gain.
For technical reasons, the in vitro biochemistry was done using human CK1 protein. There are a few places (e.g. results, line 248 and discussion line 437), where the language, in my opinion, is extrapolating the CK1 results too strongly to KIN-20. The authors mention that feedback inhibition is a known property of human CK1. It is indeed quite striking that the LIN-42 CK1BD region interacts with and is phosphorylated by the human counterpart of KIN-20, and that feedback inhibition is also seen! However, the language about KIN-20 itself should be softened, since there does not appear to be clear evidence that KIN-20 exhibits the same properties as human CK1 (unless perhaps human CK1 can functionally replace KIN-20 in worms, or the proteins were extremely similar?)
We will follow the reviewer’s advice and carefully examine the text for instances where we extrapolated too much and tone these down. (We note that this does not apply to the example of line 248 where we wrote “Collectively, our data establish that the LIN-42
CK1BD is functionally conserved and mediates stable binding to the CK1 kinase domain.”, i.e., there was no mentioning of KIN-20.)
The role of the three LIN-42 isoforms should be further clarified. Minimally, it should be explained why the alleles where both b and c isoforms should be flag-tagged seem to only produce detectable b isoform (e.g. Fig. 2C).
We will clarify that the individual roles of the isoforms are largely unknown and that we can only speculate that the c-isoform may exhibit either generally low expression or expression in only few cells or tissues.
4. Related to points 2 and 3 above, the authors have shown that the CKIBD mediates association with human CK1 in vitro, and is required for nuclear accumulation of KIN-20 in vivo, but not that the complex formation between LIN-42 and KIN-20 depends on the CK1BD. Given the reciprocal co-IP findings, it should be feasible to create tagged versions of lin-42(deltaCK1BD) and to determine the effect on LIN-42-KIN-20 complex formation. While there is already a b-isoform tag, an a-isoform tag would also help to address whether both the b and a isoforms interact with KIN-20 in a CK1BD-dependent manner in vivo. These strains would also allow the authors to determine how the CK1BD deletion affects overall levels/stability/rhythmic accumulation of LIN-42(a or b), which would potentially serve to strengthen their conclusions about the role of the lin-42 CK1BD.
We will attempt to generate a FLAG-tagged LIN-42∆CK1BD to perform IP and check for binding of KIN-20.
As detailed in section 4, we cannot tag LIN-42a individually due to the structure of the genomic locus, and its level appear very low to begin with.
In the molting timing assay, there is an unexpected result where the delta-C-terminal-tail lin-42 allele resembles the n1089 (N-terminal deletion) (line 315). Could the authors more clearly explain this finding?
As we point out in the manuscript, n1089 is a partial deletion with a breakpoint in a noncoding (intronic) region of lin-42. Accordingly, it is currently unknown, what mature transcripts and proteins are made in the mutant animals. This prevents us from making educated guesses as to why there is a phenotypic resemblance between these and lin-42∆tail mutant animals. We will clarify in the manuscript that this is an interesting, but currently unexplained observation.
*Minor comments: *
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- The correspondence between the LIN-42 "SYQ" and "LT" motifs and the motifs referred to as "A" and "B" should be clarified, and consistent names/labels used. Are these interchangeable names? If it is necessary to use both names, the differences between SYQ/LT and A/B should be made more clear.*
We agree that the situation is not completely satisfactory but feel that we need to use both names since they have both been used in the literature. We will work to revise the text to reflect more clearly the correspondence.
For data presented as "% of animals", please indicate the number of animals scored (e.g. egl, alae assays - ~ how many animals per replicate (dot)?).
We will provide these numbers.
Line 145-148 - Mentioning the relevant phenotype(s) of the lin-42 null allele from the cited paper would provide a good point of comparison here.
We will mention the previously described phenotypes.
Line 201 - the phrase "This is also true for the proteins:" is unclear, as the previous sentence states that both lin-42 and kin-20 mRNAs oscillate, while the next sentence says that only LIN-42 protein oscillates.
We apologize for the confusion and will correct the text.
Line 231 - please explain the significance of the 'lower response signal' in the BLI assay for the CKIBD(no tail).
We will clarify that the lower response signal observed for the CK1BD compared to the CK1BD+Tail (residues 402-589; same construct used in Fig. 3B) reflects its smaller molecular weight, which reduces the overall mass contribution to the BLI sensor.
Fig. 2 - C/D - the genotype lane labels should I think indicate an N-terminal rather
We will fix this mistake.
7. Fig. 6, line 367 - lin-42 is variably described as promoting increased KIN-20 'nuclear accumulation' or 'localization'. I think that 'accumulation' is more accurate, as it doesn't imply a specific mechanism for the difference (transport vs stabilization, etc.)
We will revise the manuscript accordingly.
*8. Fig 6B - an overlay of the panels or another way of quantifying the colocalization would make this result more clear. *
We will supply the requested overlay.
*Reviewer #3 (Significance (Required)): *
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This work presents a major mechanistic and conceptual advance in our understanding of the role of lin-42/Period, a conserved key regulator of C. elegans development. Previously, it was not clear if the heterochronic and circadian functions of lin-42 were genetically separable, nor was it known how LIN-42 physically interacted with the CK1 homologue. This work addresses these questions using precise genome engineering and detailed phenotypic and biochemical approaches. The work also reveals the conservation of bi-directional/reciprocal regulation between lin-42 and kin-20. The main limitations of the study, which can potentially be addressed as outlined in the 'major points' above, are that evidence should be provided that lin-42 phosphorylation depends on kin-20 in vivo, and that the CK1BD mediates the interaction in vivo (since the in vitro work is with human CK1). As the authors indicate, this is the first 'conserved clock module' of this type, and this work will therefore be of significant interest to both the C. elegans developmental biology and the more general biological timing fields. *
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Field of expertise of the reviewer- C. elegans genetics and development.*
Description of the studies that the authors prefer not to carry out
*Major comment 5 (Optional): * * In this study, the authors carefully performed in vitro kinase assays, and I strongly suggest that they investigate whether the CKI-mediated phosphorylation of LIN-42 is temperature-compensated and whether the CKI-BD-AB regions affect it. *
Temperature compensation is of course one of the most striking features of circadian clocks, and CK1-mediated phosphorylation of PER appears a critical component. We agree that it would be interesting to examine whether or not this feature exists in an animal whose development is not or only partially temperature-compensated. However, these studies are not straightforward – we would first have to set up an assay and demonstrate temperature compensation for the mammalian PER – CK1 pair as a positive control. We were not able to purify KIN-20 so could only test whether the LIN-42 substrate promoted temperature compensation. Moreover, either result for LIN-42 – CK1 would immediately raise new questions that would deserve extensive follow-up: if there is temperature compensation, why is worm development not compensated? If there is none, where/how do the interactions between CK1 and LIN-42 differ from those between CK1 and PER? Hence, we propose that these studies are outside the scope of the current study.
*Major comment 6 (Optional): * * In Figure 6, the authors argue that the CKI-BD of LIN-42 is important for CK1 nuclear translocation. It would be better to show the effect of the nuclear accumulation of CKI on nuclear proteins, like the mammalian CKI-PER2-CLOCK story. Does CKI localization affect phosphorylation status of other clock-related proteins including REV-ERB/NHR-85? * * Phospho-proteome analysis would identify nuclear substrates of CK1. In addition, is phosphorylation of LIN-42 dispensable for the CK1 nuclear translocation? *
We agree that it will be important to identify relevant targets of KIN-20 in future work. Unfortunately, at this point, none are known, and we especially do not have any knowledge of the phosphorylation status of NHR-85. Indeed, in unrelated (and unpublished) work we have done a phosphoproteomics time course of wild-type animals. We have not detected any NHR-85-derived phosphopeptides in our analysis. Thus, this would establish a completely new line of research, incompatible with the timelines of a revision.
@Ref. 3:
- *The authors have shown that LIN-42 is phosphorylated in vivo, but the dependence of this phosphorylation on KIN-20 is not fully addressed. In the discussion (lines 417-420), the authors mention that the unhealthy phenotype of the kin-20 mutant animals prevented them from assessing LIN-42 phosphorylation in this genetic background. To bolster their model and to circumvent this issue, it should be feasible to generate a kin-20 degron allele and to perform the LIN-42 phospho-proteomics upon inducible degradation. Alternatively, perhaps a phos-tag western blot for LIN-42 could be used to compare the kin-20 wild-type to kin-20 mutants. * We agree, and acknowledged in the discussion, that phoshorylation of LIN-42 by KIN-20 in vivo has not been demonstrated by us. However, since our data from the LIN-42∆Tail mutant also suggest that LIN-42 phosphorylation be functionally largely dispensable for KIN-20’s function in rhythmic molting, we consider further elucidation of this point a lower priority, especially considering the challenges involved. As we have seen for our unpublished work on wild-type animals, a phosphoproteomics experiments would be costly and time-consuming, with a non-trivial analysis (due to the underlying dynamics of protein level changes). A phos-tag gel would be subject to multiple confounders given the abundance of the phosphosites that we detected on immunoprecipitated LIN-42 – unlikely to stem only from KIN-20 activity – and an increase in total LIN-42 levels that we observe upon KIN-20 depletion, and thus appears unsuited to providing a meaningful answer.
*Related to points 2 and 3 above, the authors have shown that the CKIBD mediates association with human CK1 in vitro, and is required for nuclear accumulation of KIN-20 in vivo, but not that the complex formation between LIN-42 and KIN-20 depends on the CK1BD. Given the reciprocal co-IP findings, it should be feasible to create tagged versions of lin-42(deltaCK1BD) and to determine the effect on LIN-42-KIN-20 complex formation. While there is already a b-isoform tag, an a-isoform tag would also help to address whether both the b and a isoforms interact with KIN-20 in a CK1BD-dependent manner in vivo. These strains would also allow the authors to determine how the CK1BD deletion affects overall levels/stability/rhythmic accumulation of LIN-42(a or b), which would potentially serve to strengthen their conclusions about the role of the lin-42 CK1BD. *
As detailed in section 2, we will address the point concerning LIN-42∆CK1BD. However, due to the overlapping exons, we are unable to tag the a-isoform independently of the b-isoform. Moreover, in a western blot of a line where both a- and b-isoforms are tagged, we have observed only little or no LIN-42a signal, suggesting that, like the c-isoform, its expression may be more limited, making biochemical characterization difficult. Hence, these experiments are not feasible.
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Referee #3
Evidence, reproducibility and clarity
In their manuscript "A conserved chronobiological complex times C. elegans development", Spangler, Braun, Ashley et al. investigate the mechanisms through which the PERIOD orthologue, lin-42, regulates rhythmic molting in C. elegans. Through precise genetic manipulations, the authors identify a particular region of lin-42, the 'CK1BD', which regulates molting timing, with less effect on other lin-42 phenotypes (e.g. heterochrony). They show that LIN-42 and the casein kinase 1 (CK1) homologue KIN-20 interact in vivo, and identify phosphorylation sites of LIN-42. Using biochemical assays, they find that the CK1BD of LIN-42 is sufficient for interaction with the human homologue of KIN-20, CK1, in vitro. The LIN-42 CK1BD is also required for the proper nuclear accumulation of KIN-20 in vivo. Furthermore, a point mutation that should disrupt the catalytic activity of KIN-20 also shows an irregular molting phenotype, similar to the lin-42 CK1BD mutant. The manuscript is very well-written and the data and methods are well-presented and detailed. Overall this work makes a convincing case that the C. elegans lin-42:Kin-20 and mammalian period:Ck1 interactions have functionally conserved roles in the oscillatory developmental programs of each organism (molting timing and circadian rhythms, respectively), with a few caveats below that can be addressed.
Major comments:
- The authors have shown that LIN-42 is phosphorylated in vivo, but the dependence of this phosphorylation on KIN-20 is not fully addressed. In the discussion (lines 417-420), the authors mention that the unhealthy phenotype of the kin-20 mutant animals prevented them from assessing LIN-42 phosphorylation in this genetic background. To bolster their model and to circumvent this issue, it should be feasible to generate a kin-20 degron allele and to perform the LIN-42 phospho-proteomics upon inducible degradation. Alternatively, perhaps a phos-tag western blot for LIN-42 could be used to compare the kin-20 wild-type to kin-20 mutants.
- For technical reasons, the in vitro biochemistry was done using human CK1 protein. There are a few places (e.g. results, line 248 and discussion line 437), where the language, in my opinion, is extrapolating the CK1 results too strongly to KIN-20. The authors mention that feedback inhibition is a known property of human CK1. It is indeed quite striking that the LIN-42 CK1BD region interacts with and is phosphorylated by the human counterpart of KIN-20, and that feedback inhibition is also seen! However, the language about KIN-20 itself should be softened, since there does not appear to be clear evidence that KIN-20 exhibits the same properties as human CK1 (unless perhaps human CK1 can functionally replace KIN-20 in worms, or the proteins were extremely similar?)
- The role of the three LIN-42 isoforms should be further clarified. Minimally, it should be explained why the alleles where both b and c isoforms should be flag-tagged seem to only produce detectable b isoform (e.g. Fig. 2C).
- Related to points 2 and 3 above, the authors have shown that the CKIBD mediates association with human CK1 in vitro, and is required for nuclear accumulation of KIN-20 in vivo, but not that the complex formation between LIN-42 and KIN-20 depends on the CK1BD. Given the reciprocal co-IP findings, it should be feasible to create tagged versions of lin-42(deltaCK1BD) and to determine the effect on LIN-42-KIN-20 complex formation. While there is already a b-isoform tag, an a-isoform tag would also help to address whether both the b and a isoforms interact with KIN-20 in a CK1BD-dependent manner in vivo. These strains would also allow the authors to determine how the CK1BD deletion affects overall levels/stability/rhythmic accumulation of LIN-42(a or b), which would potentially serve to strengthen their conclusions about the role of the lin-42 CK1BD.
- In the molting timing assay, there is an unexpected result where the delta-C-terminal-tail lin-42 allele resembles the n1089 (N-terminal deletion) (line 315). Could the authors more clearly explain this finding?
Minor comments:
- The correspondence between the LIN-42 "SYQ" and "LT" motifs and the motifs referred to as "A" and "B" should be clarified, and consistent names/labels used. Are these interchangeable names? If it is necessary to use both names, the differences between SYQ/LT and A/B should be made more clear.
- For data presented as "% of animals", please indicate the number of animals scored (e.g. egl, alae assays - ~ how many animals per replicate (dot)?).
- Line 145-148 - Mentioning the relevant phenotype(s) of the lin-42 null allele from the cited paper would provide a good point of comparison here.
- Line 201 - the phrase "This is also true for the proteins:" is unclear, as the previous sentence states that both lin-42 and kin-20 mRNAs oscillate, while the next sentence says that only LIN-42 protein oscillates.
- Line 231 - please explain the significance of the 'lower response signal' in the BLI assay for the CKIBD(no tail).
- Fig. 2 - C/D - the genotype lane labels should I think indicate an N-terminal rather than C-terminal LIN-42 tag.
- Fig. 6, line 367 - lin-42 is variably described as promoting increased KIN-20 'nuclear accumulation' or 'localization'. I think that 'accumulation' is more accurate, as it doesn't imply a specific mechanism for the difference (transport vs stabilization, etc.)
- Fig 6B - an overlay of the panels or another way of quantifying the colocalization would make this result more clear.
Significance
This work presents a major mechanistic and conceptual advance in our understanding of the role of lin-42/Period, a conserved key regulator of C. elegans development. Previously, it was not clear if the heterochronic and circadian functions of lin-42 were genetically separable, nor was it known how LIN-42 physically interacted with the CK1 homologue. This work addresses these questions using precise genome engineering and detailed phenotypic and biochemical approaches. The work also reveals the conservation of bi-directional/reciprocal regulation between lin-42 and kin-20. The main limitations of the study, which can potentially be addressed as outlined in the 'major points' above, are that evidence should be provided that lin-42 phosphorylation depends on kin-20 in vivo, and that the CK1BD mediates the interaction in vivo (since the in vitro work is with human CK1). As the authors indicate, this is the first 'conserved clock module' of this type, and this work will therefore be of significant interest to both the C. elegans developmental biology and the more general biological timing fields.
Field of expertise of the reviewer- C. elegans genetics and development.
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readwrite.com readwrite.com
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Twitter publishing tools can now add a description to any tweet their users publish, not as a part of the 140 character message, but as a small machine-readable metadata field that travels along with the content.
This feels a lot like the tags in an annotation. We've thought about structured tags, and possibly the ability for different users or groups to publish different schemas for those structures. A tag or possibly a group layer could inherit one or more schemas by referencing them.
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www.biorxiv.org www.biorxiv.org
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Author response:
The following is the authors’ response to the original reviews.
Reviewer #2 (Public Review):
The authors make a compelling case for the biological need to exquisitely control RecB levels, which they suggest is achieved by the pathway they have uncovered and described in this work. However, this conclusion is largely inferred as the authors only investigate the effect on cell survival in response to (high levels of) DNA damage and in response to two perturbations - genetic knock-out or over-expression, both of which are likely more dramatic than the range of expression levels observed in unstimulated and DNA damage conditions.
In the discussion of the updated version of the manuscript, we have clarified the limits of our interpretation of the role of the uncovered regulation.
Lines 411-417: “It is worth noting that the observed decrease in cell viability upon DNA damage was detected for relatively drastic perturbations such as recB deletion and RecBCD overexpression. Verifying these observations in the context of more subtle changes in RecB levels would be important for further investigation of the biological role of the uncovered regulation mechanism. However, the extremely low numbers of RecB proteins make altering its abundance in a refined, controlled, and homogeneous across cells manner extremely challenging and would require the development of novel synthetic biology tools.”
Reviewer #3 (Public Review):
The major weaknesses include a lack of mechanistic depth, and part of the conclusions are not fully supported by the data.
(1) Mechanistically, it is still unclear why upon DNA damage, translation level of recB mRNA increases, which makes the story less complete. The authors mention in the Discussion that a moderate (30%) decrease in Hfq protein was observed in previous study, which may explain the loss of translation repression on recB. However, given that this mRNA exists in very low copy number (a few per cell) and that Hfq copy number is on the order of a few hundred to a few thousand, it's unclear how 30% decrease in the protein level should resides a significant change in its regulation of recB mRNA.
We agree that the entire mechanistic pathway controlling recB expression may be not limited to just Hfq involvement. We have performed additional experiments, proposed by the reviewer, suggesting that a small RNA might be involved (see below, response to comments 3&4). However, we consider that the full characterisation of all players is beyond the scope of this manuscript. In addition to describing the new data (see below), we expanded the discussion to explain more precisely why changes in Hfq abundance upon DNA damage may impact RecB translation.
Lines 384-391: “A modest decrease (~30%) in Hfq protein abundance has been seen in a proteomic study in E. coli upon DSB induction with ciprofloxacin (DOI: 10.1016/j.jprot.2018.03.002). While Hfq is a highly abundant protein, it has many mRNA and sRNA targets, some of which are also present in large amounts (DOI: 10.1046/j.1365-2958.2003.03734.x). As recently shown, the competition among the targets over Hfq proteins results in unequal (across various targets) outcomes, where the targets with higher Hfq binding affinity have an advantage over the ones with less efficient binding (DOI: 10.1016/j.celrep.2020.02.016). In line with these findings, it is conceivable that even modest changes in Hfq availability could result in significant changes in gene expression, and this could explain the increased translational efficiency of RecB under DNA damage conditions. “
(2) Based on the experiment and the model, Hfq regulates translation of recB gene through binding to the RBS of the upstream ptrA gene through translation coupling. In this case, one would expect that the behavior of ptrA gene expression and its response to Hfq regulation would be quite similar to recB. Performing the same measurement on ptrA gene expression in the presence and absence of Hfq would strengthen the conclusion and model.
Indeed, based on our model, we expect PtrA expression to be regulated by Hfq in a similar manner to RecB. However, the product encoded by the ptrA gene, Protease III, (i) has been poorly characterised; (ii) unlike RecB, is located in the periplasm (DOI: 10.1128/jb.149.3.1027-1033.1982); and (iii) is not involved in any DNA repair pathway. Therefore, analysing PtrA expression would take us away from the key questions of our study.
(3) The authors agree that they cannot exclude the possibility of sRNA being involved in the translation regulation. However, this can be tested by performing the imaging experiments in the presence of Hfq proximal face mutations, which largely disrupt binding of sRNAs.
(4) The data on construct with a long region of Hfq binding site on recB mRNA deleted is less convincing. There is no control to show that removing this sequence region itself has no effect on translation, and the effect is solely due to the lack of Hfq binding. A better experiment would be using a Hfq distal face mutant that is deficient in binding to the ARN motifs.
We performed the requested experiments. We included this data in the manuscript in the supplementary figure (Figure S11), and our interpretation in the discussion.
Lines 354-378: “While a few recent studies have shown evidence for direct gene regulation by Hfq in a sRNA-independent manner (DOI: 10.1101/gad.302547.117; DOI: 10.1111/mmi.14799; DOI: 10.1371/journal.pgen.1004440; DOI: 10.1111/mmi.12961; DOI: 10.1038/emboj.2013.205), we attempted to investigate whether a small RNA could be involved in the Hfq-mediated regulation of RecB expression. We tested Hfq mutants containing point mutations in the proximal and distal sides of the protein, which were shown to disrupt either binding with sRNAs or with ARN motifs of mRNA targets, respectively [DOI: 10.1016/j.jmb.2013.01.006, DOI: 10.3389/fcimb.2023.1282258]. Hfq mutated in either proximal (K56A) or distal (Y25D) faces were expressed from a plasmid in a ∆hfq background. In both cases, Hfq expression was confirmed with qPCR and did not affect recB mRNA levels (Supplementary Figure S11b). When the proximal Hfq binding side (K56A) was disrupted, RecB protein concentration was nearly similar to that obtained in a ∆hfq mutant (Supplementary Figure S11a, top panel). This observation suggests that the repression of RecB translation requires the proximal side of Hfq, and that a small RNA is likely to be involved as small RNAs (Class I and Class II) were shown to predominantly interact with the proximal face of Hfq [DOI: 10.15252/embj.201591569]. When we expressed Hfq mutated in the distal face (Y25D) which is deficient in binding to mRNAs, less efficient repression of RecB translation was detected (Supplementary Figure S11a, bottom panel). This suggests that RecB mRNA interacts with Hfq at this position. We did not observe full de-repression to the ∆hfq level, which might be explained by residual capacity of Hfq to bind its recB mRNA target in the point mutant (Y25D) (either via the distal face with less affinity or via the lateral rim Hfq interface).”
Taken together, these results suggest that Hfq binds to recB mRNA and that a small RNA might contribute to the regulation although this sRNA has not been identified.
(5) Ln 249-251: The authors claim that the stability of recB mRNA is not changed in ∆hfq simply based on the steady-state mRNA level. To claim so, the lifetime needs to be measured in the absence of Hfq.
We measured recB lifetime in the absence of Hfq in a time-course experiment where transcription initiation was inhibited with rifampicin and mRNA abundance was quantified with RT-qPCR. The results confirmed that recB mRNA lifetime in hfq mutants is similar to the one in the wild type (Figure S7d, referred to the line 263 of the manuscript).
(6) What's the labeling efficiency of Halo-tag? If not 100% labeled, is it considered in the protein number quantification? Is the protein copy number quantification through imaging calibrated by an independent method? Does Halo tag affect the protein translation or degradation?
Our previous study (DOI: 10.1038/s41598-019-44278-0) described a detailed characterization of the HaloTag labelling technique for quantifying low-copy proteins in single E. coli cells using RecB as a test case.
In that study, we showed complete quantitative agreement of RecB quantification between two fully independent methods: HaloTag-based labelling with cell fixation and RecB-sfGFP combined with a microfluidic device that lowers protein diffusion in the bacterial cytoplasm. This second method had previously been validated for protein quantification (DOI: 10.1038/ncomms11641) and provides detection of 80-90% of the labelled protein. Additionally, in our protocol, immediate chemical fixation of cells after the labelling and quick washing steps ensure that new, unlabelled RecB proteins are not produced. We, therefore, conclude that our approach to RecB detection is highly reliable and sufficient for comparing RecB production in different conditions and mutants.
The RecB-HaloTag construct has been designed for minimal impact on RecB production and function. The HaloTag is translationally fused to RecB in a loop positioned after the serine present at position 47 where it is unlikely to interfere with (i) the formation of RecBCD complex (based on RecBCD structure, DOI: 10.1038/nature02988), (ii) the initiation of translation (as it is far away from the 5’UTR and the beginning of the open reading frame) and (iii) conventional C-terminalassociated mechanisms of protein degradation (DOI: 10.15252/msb.20199208). In our manuscript, we showed that the RecB-HaloTag degradation rate is similar to the dilution rate due to bacterial growth. This is in line with a recent study on unlabelled proteins, which shows that RecB’s lifetime is set by the cellular growth rate (DOI: 10.1101/2022.08.01.502339).
Furthermore, we have demonstrated (DOI: 10.1038/s41598-019-44278-0) that (i) bacterial growth is not affected by replacing the native RecB with RecB-HaloTag, (ii) RecB-HaloTag is fully functional upon DNA damage, and (iii) no proteolytic processing of the RecB-HaloTag is detected by Western blot.
These results suggest that RecB expression and functionality are unlikely to be affected by the translational HaloTag insertion at Ser-47 in RecB.
In the revised version of the manuscript, we have added information about the construct and discuss the reliability of the quantification.
Lines 141-152: “To determine whether the mRNA fluctuations we observed are transmitted to the protein level, we quantified RecB protein abundance with singlemolecule accuracy in fixed individual cells using the Halo self-labelling tag (Fig. 2A&B).
The HaloTag is translationally fused to RecB in a loop after Ser47(DOI: 10.1038/s41598-019-44278-0) where it is unlikely to interfere with the formation of RecBCD complex (DOI: 10.1038/nature02988), the initiation of translation and conventional C-terminal-associated mechanisms of protein degradation (DOI: 10.15252/msb.20199208). Consistent with minimal impact on RecB production and function, bacterial growth was not affected by replacing the native RecB with RecBHaloTag, the fusion was fully functional upon DNA damage and no proteolytic processing of the construct was detected (DOI: 10.1038/s41598-019-44278-0). To ensure reliable quantification in bacteria with HaloTag labelling, the technique was previously verified with an independent imaging method and resulted in > 80% labelling efficiency (DOI: 10.1038/s41598-019-44278-0, DOI: 10.1038/ncomms11641). In order to minimize the number of newly produced unlabelled RecB proteins, labelling and quick washing steps were followed by immediate chemical fixation of cells.”
Lines 164-168: “Comparison to the population growth rate [in these conditions (0.017 1/min)] suggests that RecB protein is stable and effectively removed only as a result of dilution and molecule partitioning between daughter cells. This result is consistent with a recent high-throughput study on protein turnover rates in E. coli, where the lifetime of RecB proteins was shown to be set by the doubling time (DOI: 10.1038/s41467-024-49920-8).”
(7) Upper panel of Fig S8a is redundant as in Fig 5B. Seems that Fig S8d is not described in the text.
We have now stated in the legend of Fig S8a that the data in the upper panel were taken from Fig 5B to visually facilitate the comparison with the results given in the lower panel. We also noticed that we did not specify that in the upper panel in Fig S9a (the data in the upper panel of Fig S9a was taken from Fig 5C for the same reason). We added this clarification to the legend of the Fig S9 as well.
We referred to the Fig S8d in the main text.
Lines 283-284: “We confirmed the functionality of the Hfq protein expressed from the pQE-Hfq plasmid in our experimental conditions (Fig. S8d).”
Reviewer #1 (Recommendations For The Authors):
(1) Experimental regime to measure protein and mRNA levels.
(a) Authors expose cells to ciprofloxacin for 2 hrs. They provide a justification via a mathematical model. However, in the absence of a measurement of protein and mRNA across time, it is unclear whether this single time point is sufficient to make the conclusion on RecB induction under double-strand break.
In our experiments, we only aimed to compare recB mRNA and RecB protein levels in two steady-state conditions: no DNA damage and DNA damage caused by sublethal levels of ciprofloxacin. We did not aim to look at RecB dynamic regulation from nondamaged to damaged conditions – this would indeed require additional measurements at different time points. We revised this part of the results to ensure that our conclusions are stated as steady-state measurements and not as dynamic changes.
Line 203-205: “We used mathematical modelling to verify that two hours of antibiotic exposure was sufficient to detect changes in mRNA and protein levels and for RecB mRNA and protein levels to reach a new steady state in the presence of DNA damage.”
(b) Authors use cell area to account for the elongation under damage conditions. However, it is unclear whether the number of copies of the recB gene are similar across these elongated cells. Hence, authors should report mRNA and protein levels with respect to the number of gene copies of RecB or chromosome number as well.
Based on the experiments in DNA damaging conditions, our main conclusion is that the average translational efficiency of RecB is increased in perturbed conditions. We believe that this conclusion is well supported by our measurements and that it does not require information about the copy number of the recB gene but only the concentration of mRNA and protein. We did observe lower recB mRNA concentration upon DNA damage in comparison to the untreated conditions, which may be due to a lower concentration of genomic DNA in elongated cells upon DNA damage, as we mention in lines (221-223).
Our calculation of translation efficiency could be affected by variations of mRNA concentration across cells in the dataset. For example, longer cells that are potentially more affected by DNA damage could have lower concentrations of mRNA. We verified that this is not the case, as recB mRNA concentration is constant across cell size distribution (see the figure below or Figure S5a from Supplementary Information).
Therefore, we do not think that the measurements of recB gene copy would change our conclusions. We agree that measuring recB gene copies could help to investigate the reason behind the lower recB mRNA concentration under the perturbed conditions as this could be due to lower DNA content or due to shortage of resources (such as RNA polymerases). However, this is a side observation we made rather than a critical result, whose investigation is beyond the scope of this manuscript.
Author response image 1.
(2) RecB as a proxy for RecBCD. Authors suggest that RecB levels are regulated by hfq. However, how does this regulatory circuit affect the levels of RecC and RecD? Ratio of the three proteins has been shown to be important for the function of the complex.
A full discussion of RecBCD complex formation regulation would require a complete quantitative model based on precise information on the dynamic of the complex formation, which is currently lacking.
We can however offer the following (speculative) suggestions assuming that all three subunits are present in similar abundance in native conditions (DOI: 10.1038/s41598019-44278-0 for RecB and RecC). As the complex is formed in 1:1:1 ratio (DOI: 10.1038/nature02988), we propose that the regulation mechanism of RecB expression affects complex formation in the following way. If the RecB abundance becomes lower than the level of RecC and RecD subunits, the complex formation would be limited by the number of available RecB subunits and hence the number of functional RecBCDs will be decreased. On the contrary, if the number of RecB is higher than the baseline, then, especially in the context of low numbers, we would expect that the probability of forming a complex RecBC (and then RecBCD) will be increased. Based on this simple explanation, we might speculate that regulation of RecB expression may be sufficient to regulate RecB levels and RecBCD complex formation. However, we feel that this argument is too speculative to be added to the manuscript.
(3) Role of Hfq in RecB regulation. While authors show the role of hfq in recB translation regulation in non-damage conditions, it is unclear as to how this regulation occurs under damage conditions.
(a) Have the author carried out recB mRNA and protein measurement in hfqdeleted cells under ciprofloxacin treatment?
We attempted to perform experiments in hfq mutants under ciprofloxacin treatment. However, the cells exhibited a very strong and pleiotropic phenotype: they had large size variability and shape changes and were also frequently lysing. Therefore, we did not proceed with mRNA and protein quantification because the data would not have been reliable.
(b) How do the authors propose that Hfq regulation is alleviated under conditions of DNA damage, when RecB translation efficiency increases?
We propose that Hfq could be involved in a more global response to DNA damage as follows.
Based on a proteomic study where Hfq protein abundance has been found to decrease (~ 30%) upon DSB induction with ciprofloxacin (DOI: 10.1016/j.jprot.2018.03.002), we suggest that this could explain the increased translational efficiency of RecB. While Hfq is a highly abundant protein, it has many targets (mRNA and sRNA), some of which are also highly abundant. Therefore the competition among the targets over Hfq proteins results in unequal (across various targets) outcomes (DOI: 10.1046/j.13652958.2003.03734.x), where the targets with higher Hfq binding affinity have an advantage over the ones with less efficient binding. We reason that upon DNA damage, a moderate decrease in the Hfq protein abundance (30%) can lead to a similar competition among Hfq targets where high-affinity targets outcompete low-affinity ones as well as low-abundant ones (such as recB mRNAs). Thus, the regulation of lowabundant targets of Hfq by moderate perturbations of Hfq protein level is a potential explanation for the change in RecB translation that we have observed. Potential reasons behind the changes of Hfq levels upon DNA damage would be interesting to explore, however this would require a completely different approach and is beyond the scope of this manuscript.
We have modified the text of the discussion to explain our reasoning:
Lines 384-391: “A modest decrease (~30%) in Hfq protein abundance has been seen in a proteomic study in E. coli upon DSB induction with ciprofloxacin (DOI: 10.1016/j.jprot.2018.03.002). While Hfq is a highly abundant protein, it has many mRNA and sRNA targets, some of which are also present in large amounts (DOI: 10.1046/j.1365-2958.2003.03734.x). As recently shown, the competition among the targets over Hfq proteins results in unequal (across various targets) outcomes, where the targets with higher Hfq binding affinity have an advantage over the ones with less efficient binding (DOI: 10.1016/j.celrep.2020.02.016). In line with these findings, it is conceivable that even modest changes in Hfq availability could result in significant changes in gene expression, and this could explain the increased translational efficiency of RecB under DNA damage conditions.”
(c) Is there any growth phenotype associated with recB mutant where hfq binding is disrupted in damage and non-damage conditions? Does this mutation affect cell viability when over-expressed or under conditions of ciprofloxacin exposure?
We checked the phenotype and did not detect any difference in growth or cell viability affecting the recB-5 UTR* mutants either in normal conditions or upon exposure to ciprofloxacin. However, this is expected because the repair capacity is associated with RecB protein abundance and in this mutant, while translational efficiency of recB mRNA increases, the level of RecB proteins remains similar to the wild-type (Figure 5E).
Minor points:
(1) Introduction - authors should also discuss the role of RecFOR at sites of fork stalling, a likely predominant pathway for break generated at such sites.
The manuscript focuses on the repair of DNA double-strand breaks (DSBs). RecFOR plays a very important role in the repair of stalled forks because of single-strand gaps but is not involved in the repair of DSBs (DOI: 10.1038/35003501). We have modified the beginning of the introduction to mention the role of RecFOR.
Lines 35-39: “For instance, replication forks often encounter obstacles leading to fork reversal, accumulation of gaps that are repaired by the RecFOR pathway (DOI: 10.1038/35003501) or breakage which has been shown to result in spontaneous DSBs in 18% of wild-type Escherichia coli cells in each generation (DOI: 10.1371/journal.pgen.1007256), underscoring the crucial need to repair these breaks to ensure faithful DNA replication.”
(2) Methods: The authors refer to previous papers for the method used for single RNA molecule detection. More information needs to be provided in the present manuscript to explain how single molecule detection was achieved.
We added additional information in the method section on the fitting procedure allowing quantifying the number of mRNAs per detected focus.
Lines 515-530: “Based on the peak height and spot intensity, computed from the fitting output, the specific signal was separated from false positive spots (Fig. S1a). To identify the number of co-localized mRNAs, the integrated spot intensity profile was analyzed as previously described (DOI: 10.1038/nprot.2013.066). Assuming that (i) probe hybridization is a probabilistic process, (ii) binding each RNA FISH probe happens independently, and (iii) in the majority of cases, due to low-abundance, there is one mRNA per spot, it is expected that the integrated intensities of FISH probes bound to one mRNA are Gaussian distributed. In the case of two co-localized mRNAs, there are two independent binding processes and, therefore, a wider Gaussian distribution with twice higher mean and twice larger variance is expected. In fact, the integrated spot intensity profile had a main mode corresponding to a single mRNA per focus, and a second one representing a population of spots with two co-localized mRNAs (Fig. S1b). Based on this model, the integrated spot intensity histograms were fitted to the sum of two Gaussian distributions (see equation below where a, b, c, and d are the fitting parameters), corresponding to one and two mRNA molecules per focus. An intensity equivalent corresponding to the integrated intensity of FISH probes in average bound to one mRNA was computed as a result of multiple-Gaussian fitting procedure (Fig. S1b), and all identified spots were normalized by the one-mRNA equivalent.
Reviewer #2 (Recommendations For The Authors):
Overall the work is carefully executed and highly compelling, providing strong support for the conclusions put forth by the authors.
One point: the potential biological consequences of the post-transcriptional mechanism uncovered in the work would be enhanced if the authors could 1) tune RecB protein levels and 2) directly monitor the role that RecB plays in generating single-standed DNA at DSBs.
We agree that testing viability of cells in case of tunable changes in RecB levels would be important to further investigate the biological role of the uncovered regulation mechanism. However, this is a very challenging experiment as it is technically difficult to alter the low number of RecB proteins in a controlled and homogeneous across-cell manner, and it would require the development of precisely tunable and very lowabundant synthetic designs.
We did monitor real-time RecB dynamics by tracking single molecules in live E. coli cells in a different study (DOI: 10.1101/2023.12.22.573010) that is currently under revision. There, reduced motility of RecB proteins was observed upon DSB induction indicating that RecB is recruited to DNA to start the repair process.
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content-security-policy.com content-security-policy.com
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Example a CSP header with a meta tag
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huggingface.co huggingface.co
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Docker setup Installation Install Docker on your system Install the required packages: Copied pip install 'smolagents[docker]' Setting up the docker sandbox Create a Dockerfile for your agent environment: Copied FROM python:3.10-bullseye # Install build dependencies RUN apt-get update && \ apt-get install -y --no-install-recommends \ build-essential \ python3-dev && \ pip install --no-cache-dir --upgrade pip && \ pip install --no-cache-dir smolagents && \ apt-get clean && \ rm -rf /var/lib/apt/lists/* # Set working directory WORKDIR /app # Run with limited privileges USER nobody # Default command CMD ["python", "-c", "print('Container ready')"] Create a sandbox manager to run code: Copied import docker import os from typing import Optional class DockerSandbox: def __init__(self): self.client = docker.from_env() self.container = None def create_container(self): try: image, build_logs = self.client.images.build( path=".", tag="agent-sandbox", rm=True, forcerm=True, buildargs={}, # decode=True ) except docker.errors.BuildError as e: print("Build error logs:") for log in e.build_log: if 'stream' in log: print(log['stream'].strip()) raise # Create container with security constraints and proper logging self.container = self.client.containers.run( "agent-sandbox", command="tail -f /dev/null", # Keep container running detach=True, tty=True, mem_limit="512m", cpu_quota=50000, pids_limit=100, security_opt=["no-new-privileges"], cap_drop=["ALL"], environment={ "HF_TOKEN": os.getenv("HF_TOKEN") }, ) def run_code(self, code: str) -> Optional[str]: if not self.container: self.create_container() # Execute code in container exec_result = self.container.exec_run( cmd=["python", "-c", code], user="nobody" ) # Collect all output return exec_result.output.decode() if exec_result.output else None def cleanup(self): if self.container: try: self.container.stop() except docker.errors.NotFound: # Container already removed, this is expected pass except Exception as e: print(f"Error during cleanup: {e}") finally: self.container = None # Clear the reference # Example usage: sandbox = DockerSandbox() try: # Define your agent code agent_code = """ import os from smolagents import CodeAgent, HfApiModel # Initialize the agent agent = CodeAgent( model=HfApiModel(token=os.getenv("HF_TOKEN"), provider="together"), tools=[] ) # Run the agent response = agent.run("What's the 20th Fibonacci number?") print(response) """ # Run the code in the sandbox output = sandbox.run_code(agent_code) print(output) finally: sandbox.cleanup()
docker e2b sandbox
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www.biorxiv.org www.biorxiv.org
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Author response:
The following is the authors’ response to the previous reviews.
Public Reviews:
Reviewer #1 (Public review):
Comment of Review of Revised Version:
Although the authors have partly corrected the manuscript by removing the mislabeling in their Co-IP experiments, my primary concern on the actual functional connotations and direct interaction between PA28y and C1QBP still remains unaddressed. As already mentioned in my previous review, since the core idea of the work is PA28y's direct interaction with C1QBP, stabilizing it, the same should be demonstrated in a more convincing manner.
My other observation on the detection of C1QBP as a doublet has been addressed by usage of anti-C1QBP Monoclonal antibody against the polyclonal one used before. C1QBP doublets have not been observed in the present case.
The authors have also worked on the presentation of the background by suitably modifying the statements and incorporating appropriate citations.
However, the authors are requested to follow the recommendations provided to them by the reviewers to address the major concerns.
Thank you very much for your comments. We appreciate your concerns regarding the need for more direct evidence to support the stabilizing interaction between PA28γ and C1QBP. In response to your feedback, we have taken additional steps to provide more convincing evidence of this interaction.
To complement our existing pull-down and Co-IP experiments, we utilized AlphaFold 3 to predict the three-dimensional structure of the PA28γ-C1QBP complex. The predicted model reveals specific residues and interfaces that are likely involved in the direct interaction between PA28γ and C1QBP. Our analysis indicates that this interaction may depend on amino acids 1-167 and 1-213 of C1QBP (Revised Appendix Figure 1E-H). Furthermore, aspartate (ASP), as the 177th amino acids of PA28γ, was predicted to interact with the 76th amino acid threonine (THR) and the 78th amino acid glycine (GLY) of C1QBP (Revised Appendix Figure 1I). This structural insight was further validated by our immunoprecipitation experiments (Revised Figure 1J). These findings provide a molecular basis for the observed stabilizing effect and suggest potential mechanisms by which PA28γ influences C1QBP stability. Specifically, the identified interaction sites offer clues into how PA28γ may stabilize C1QBP at the molecular level.
Furthermore, we performed proximity ligation assays (PLA) to detect in situ interactions between PA28γ and C1QBP at the single-cell level. PLA results clearly demonstrate the presence of PA28γ-C1QBP complexes within cells, providing direct evidence of their physical interaction (Revised Figure 1D). This approach overcomes some of the limitations associated with traditional IP experiments and confirms the direct nature of the interaction.
In summary, the integration of AlphaFold 3 predictions, PLA data, and our previous Pull-down and Co-IP experiments provides robust and direct evidence for a stable interaction between PA28γ and C1QBP. We believe that these additional findings significantly reinforce our conclusions and effectively address the concerns raised by the reviewers. Once again, thank you for your valuable feedback, which has been instrumental in refining and enhancing our study.
Reviewer #2 (Public review):
Comment of Review of Revised Version:
Weaknesses:
Many data sets are shown in figures that cannot be understood without more descriptions either in the text or the legend, e.g., Fig. 1A. Similarly, many abbreviations are not defined.
The revision addressed these issues.
Some of the pull-down and coimmunoprecipitation data do not support the conclusion about the PA28g-C1QBP interaction. For example, in Appendix Fig. 1B the Flag-C1QBP was detected in the Myc beads pull-down when the protein was expressed in the 293T cells without the Myc-PA28g, suggesting that the pull-down was not due to the interaction of the C1QBP and PA28g proteins. In Appendix Fig. 1C, assume the SFB stands for a biotin tag, then the SFB-PA28g should be detected in the cells expressing this protein after pull-down by streptavidin; however, it was not. The Western blot data in Fig. 1E and many other figures must be quantified before any conclusions about the levels of proteins can be drawn.
The revision addressed these problems.
The immunoprecipitation method is flawed as it is described. The antigen (PA28g or C1QBP) should bind to the respective antibody that in turn should binds to Protein G beads. The resulting immunocomplex should end up in the pellet fraction after centrifugation, and analyzed further by Western blot for coprecipitates. However, the method in the Appendix states that the supernatant was used for the Western blot.
The revision corrected this method.
To conclude that PA28g stabilizes C1QBP through their physical interaction in the cells, one must show whether a protease inhibitor can substitute PA28q and prevent C1QBP degradation, and also show whether a mutation that disrupt the PA28g-C1QBP interaction can reduce the stability of C1QBP. In Fig. 1F, all cells expressed Myc-PA28g. Therefore, the conclusion that PA28g prevented C1QBP degradation cannot be reached. Instead, since more Myc-PA28g was detected in the cells expressing Flag-C1QBP compared to the cells not expressing this protein, a conclusion would be that the C1QBP stabilized the PA28g. Fig. 1G is a quantification of a Western blot data that should be shown.
The binding site for PA28g in C1QBP was mapped to the N-terminal 167 residues using truncated proteins. One caveat would be that some truncated proteins did not fold correctly in the absence of the sequence that was removed. Thus, the C-terminal region of the C1QBP with residues 168-283 may still bind to the PA29g in the context of full-length protein. In Fig. 1I, more Flag-C1QBP 1-167 was pull-down by Myc-PA28g than the full-length protein or the Flag-C1QBP 1-213. Why?
The interaction site in PA28g for C1QBP was not mapped, which prevents further analysis of the interaction. Also, if the interaction domain can be determined, structural modeling of the complex would be feasible using AlphaFold2 or other programs. Then, it is possible to test point mutations that may disrupt the interaction and if so, the functional effect.
The revision added AlphaFold models for the protein interaction. However, the models were not analyzed and potential mutations that would disrupt the interact were not predicted, made and tested. The revision did not addressed the request for the protease inhibitor.
Thank you for your insightful comments regarding the binding site of PA28γ in C1QBP. We appreciate your concern about the potential misfolding of truncated proteins and the possible interaction between the C-terminal region (residues 168-283) of C1QBP and PA28γ in the context of full-length protein.
To address these concerns, we have conducted additional analyses and experiments to provide a more comprehensive understanding of the interaction between PA28γ and C1QBP. Using AlphaFold 3, we predicted the three-dimensional structure of the PA28γ-C1QBP complex. The model reveals specific residues and interfaces that are likely involved in the direct interaction between PA28γ and C1QBP. Notably, our structural analysis indicates that the interaction may primarily depend on amino acids 1-167 and 1-213 of C1QBP (Revised Appendix Figure 1E-H). Furthermore, aspartate (ASP), as the 177th amino acids of PA28γ, was predicted to interact with the 76th amino acid threonine (THR) and the 78th amino acid glycine (GLY) of C1QBP (Revised Appendix Figure 1I). This prediction supports the idea that the N-terminal region of C1QBP is crucial for its interaction with PA28γ. Regarding the observation in old Figure 1I (Revised Figure 1J), where more Flag-C1QBP 1-167 was pulled down by Myc-PA28γ compared to the full-length protein or Flag-C1QBP 1-213, we believe this can be explained by several factors:
A. The truncation of C1QBP to residues 1-167 may expose key interaction sites that are partially obscured in the full-length protein. This enhanced accessibility could lead to stronger binding affinity and higher pull-down efficiency.
B. While it is possible that some truncated proteins do not fold correctly, our data suggest that the N-terminal fragment (1-167) retains sufficient structural integrity to interact effectively with PA28γ. The increased pull-down of this fragment suggests that it captures the essential elements required for binding.
C. The C-terminal region (168-283) might exert steric hindrance or allosteric effects on the N-terminal binding site in the context of the full-length protein. This interference could reduce the overall binding efficiency, leading to less pull-down of full-length C1QBP compared to the truncated version.
Compared with the control group, the presence of Myc-PA28γ significantly increased the expression level of Flag-C1QBP (r Revised Figure 1G). Gray value analysis showed that in cells transfected with Myc-PA28γ, the decay rate of Flag-C1QBP was significantly slower than that of the control group (Revised Figure 1H), suggesting that PA28γ can delay the protein degradation of C1QBP and stabilize its protein level. This indicates that an increase in the level of PA28γ protein can significantly enhance the expression level of C1QBP protein, while PA28γ can slow down the degradation rate of C1QBP and improve its stability. In addition, our western blot analysis also proved that PA28γ could still prevent the degradation of C1QBP under the action of proteasome inhibitor MG-132 (Revised Appendix Figure 1D). Moreover, PA28γ could not stabilize the mutation of C-terminus of C1QBP (amino acids 94-282), which was not the interaction domain of PA28γ-C1QBP (Revised Figure 1K).
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Author response:
The following is the authors’ response to the original reviews.
Reviewer #1 (Public review):
Summary:
This manuscript presents evidence of ’vocal style’ in sperm whale vocal clans. Vocal style was defined as specific patterns in the way that rhythmic codas were produced, providing a fine-scale means of comparing coda variations. Vocal style effectively distinguished clans similar to the way in which vocal repertoires are typically employed. For non-identity codas, vocal style was found to be more similar among clans with more geographic overlap. This suggests the presence of social transmission across sympatric clans while maintaining clan vocal identity.
Strengths:
This is a well-executed study that contributes exciting new insights into cultural vocal learning in sperm whales. The methodology is sound and appropriate for the research question, building on previous work and ground-truthing much of their theories. The use of the Dominica dataset to validate their method lends strength to the concept of vocal style and its application more broadly to the Pacific dataset. The results are framed well in the context of previous works and clearly explain what novel insights the results provide to the current understanding of sperm whale vocal clans. The discussion does an overall great job of outlining why horizontal social learning is the best explanation for the results found.
Weaknesses:
The primary issues with the manuscript are in the technical nature of the writing and a lack of clarity at times with certain terminology. For example, several tree figures are presented and ’distance’ between trees is key to the results, yet ’distance’ is not clearly defined in a way for someone unfamiliar with Markov chains to understand. However, these are issues that can easily be dealt with through minor revisions with a view towards making the manuscript more accessible to a general audience.
I also feel that the discussion could focus a bit more on the broader implications - specifically what the developed methods and results might imply about cultural transmission in other species. This is specifically mentioned in the abstract but not really delved into in detail during the discussion.
We are grateful for the Reviewer’s recognition of the study’s contributions to understanding cultural vocal learning in sperm whales. In response to the concerns regarding clarity and accessibility, we have revised the manuscript to improve the definition of key concepts, such as the notion of “distance” between subcoda trees. This adjustment ensures clarity for readers unfamiliar with the technical details of Markov chains. Additionally, we have expanded the discussion to highlight broader implications of our findings, particularly their relevance to understanding cultural transmission in other species, as suggested.
Reviewer #2 (Public review):
Summary:
The current article presents a new type of analytical approach to the sequential organisation of whale coda units.
Strengths:
The detailed description of the internal temporal structure of whale codas is something that has been thus far lacking.
Weaknesses:
It is unclear how the insight gained from these analyses differs or adds to the voluminous available literature on how codas varies between whale groups and populations. It provides new details, but what new aspects have been learned, or what features of variation seem to be only revealed by this new approach? The theoretical basis and concepts of the paper are problematical and indeed, hamper potentially the insights into whale communication that the methods could offer. Some aspects of the results are also overstated.
We appreciate the Reviewer’s acknowledgment of the novelty in describing the internal temporal structure of whale codas. Regarding the concern about the unique contributions of this approach, we have further emphasized in the revised manuscript how our methodology reveals previously uncharacterized dimensions of coda structure. Specifically, our work highlights how non-identity codas, which have received limited attention, play a significant role in inter-clan acoustic interactions. By leveraging Variable Length Markov Chains, we provide a nuanced understanding of coda subunits that complements existing studies and demonstrates the value of this analytical approach.
Reviewer #3 (Public review):
Summary:
The study presented by Leitao et al., represents an important advancement in comprehending the social learning processes of sperm whales across various communicative and socio-cultural contexts. The authors introduce the concept of ”vocal style” as an addition to the previously established notion of ”vocal repertoire,” thereby enhancing our understanding of sperm whale vocal identity.
Strengths:
A key finding of this research is the correlation between the similarity of clan vocal styles for non-ID codas and spatial overlap (while no change occurs for ID codas), suggesting that social learning plays a crucial role in shaping symbolic cultural boundaries among sperm whale populations. This work holds great appeal for researchers interested in animal cultures and communication. It is poised to attract a broad audience, including scholars studying animal communication and social learning processes across diverse species, particularly cetaceans.
Weaknesses:
In terms of terminology, while the authors use the term ”saying” to describe whale vocalizations, it may be more conservative to employ terms like ”vocalize” or ”whale speech” throughout the manuscript. This approach aligns with the distinction between human speech and other forms of animal communication, as outlined in prior research (Hockett, 1960; Cheney & Seyfarth, 1998; Hauser et al., 2002; Pinker & Jackendoff, 2005; Tomasello, 2010).
We thank the Reviewer for recognizing the importance of our findings and their appeal to broader audiences interested in animal cultures and communication. In response to the suggestion regarding terminology, we have adopted a more conservative language to align with distinctions between human and non-human communication systems. For example, terms like “vocalize” and “vocal repertoire” are used in place of anthropomorphic terms such as “saying”. This ensures consistency with established conventions while maintaining clarity for a broad readership.
Reviewer #1 (Recommendations):
Comment 1
Lines 11-13: As mentioned above, the implications for comparing communication systems and cultural transmission in other species isn’t really discussed much and I think it’s a really interesting component of the study’s broader implications.
Thank you for the comment.
Action - We added a few more sentences to the discussion regarding this.
Comment 2
Figure 1: More information on the figure of these trees would help. What do the connecting lines represent? What do the plain black dots and the black dot with the white dot represent? Especially since the ”distance between trees” is a key result, it’s important that someone unfamiliar with Markov chains can understand the basics of how this is calculated and what it represents. It is explained in the methods, but a brief explanation here would make the results and the figure a lot clearer since the methods are the last section of the manuscript.
These were omitted as we believed that attempting to introduce the mathematical structure and the methodology to compare two instances, in a figure caption, would have caused more ambiguity than necessary.
Action - Added an informal introduction to these concepts on the figure caption. Also added a pointer to the Supplementary Materials.
Comment 3
Table 1: A definition of dICIs should be included here.
Added the definition of discrete ICI to the table.
Comment 4
Figure 2: The placement of the figures is a bit confusing because they are quite far from the text that references them.
We thank the reviewer for pointing this out, we tried to edit the manuscript to improve this issue, but this part of the editing is more within the journal’s powers than our own.
Action - Moved images closes to the corresponding text in manuscript.
Comment 5
Line 117: Probabilistic distance needs to be briefly explained earlier when you first mention distance (see Lines 11-13 comments).
Action - Clarifications added in the caption of figure 1. as per comment on Lines 11-13
Comment 6
Figure 4: Is order considered in these pairwise comparisons? It looks like there are two dots for each pairwise comparison. Additionally, why is the overlap different in these two comparisons? For example, short:four-plus has an overlap of 0.6, while four-plus:short has an overlap of 0.95.
The x-axis of the plots in Figure 4 is geographical clan overlap. This is calculated as per (Hersh et al., 2022) and is described in our Methods (see “Measuring clan overlap” section). Given two clans—for example, the Four-Plus and the Short clan—spatial overlap is calculated twice: as the proportion of the Four-Plus clan’s repertoires that were recorded within 1,000 km of at least one of the Short clan’s repertoires, and as the proportion of the Short clan’s repertoires that were recorded within 1,000 km of at least one of the Four-Plus clan’s repertoires.
Order is important in these pairwise comparisons and generates an asymmetric matrix because the clans have different spatial extents. A clan found in only one small region might overlap completely with a clan that spans the Pacific Ocean, while the opposite is not true. For example, the Short clan spans the Pacific Ocean while the Four-Plus clan has been documented over a smaller area (but that smaller area overlaps extensively with the Short clan range). That is why the value is smaller (0.6) when considering how much of the Short clan’s range is shared with the Four-Plus clan, and larger ( 0.95) when considering how much of the Four-Plus clan’s range is shared with the Short clan.
Action - We have now added a reference to that section of the Methods in our Figure 4 caption and include the clan spatial overlap matrix as a supplemental table (Table S5).
Comment 7
Figure 4: I think the reference should be Hersh et al. [11].
Thank you for catching this.
Action - Reference corrected
Comment 8
Line 227: What aspect of your analysis looked at how often codas were produced? You mention coda frequency, but it is unclear how this was incorporated into your analysis. If this is included in the methods, the language is a bit too technical to easily parse it out.
Indeed here we are referencing the results of the paper mentioned in the previous line. We do not look at coda production frequency.
Action - Added citation to paper that actually performs this analysis.
Comment 9
Lines 253-255: I think you could dig into this a little more, as ”there is currently no evidence” is not the most convincing argument that something is not a driver. Perhaps expanding on the latter sentence that clans are recognizable across oceans basins would be helpful. Does this suggest that clans with similar geographic overlap experience diverse environmental conditions across ocean basins? If so, this might better strengthen your argument against environmental drivers.
Thank you for pointing this out. We feel that the next sentence highlights that clans are recognizable across environmental variation from one side to the other of the ocean basin, which supports the inductive reasoning that codas do not vary systematically with environment. However, we have edited these sentences for clarity.
Comment 10
Lines 311-314: It would also be interesting to look at vocal style across non-ID coda types. Are some more similar to each other across clans than others? Perhaps vocal style can further distinguish types of non-ID codas.
In supplementary Materials 3.4.2 and 3.5 we highlight our results when the codas are separated by coda type summarized in Table S4. We do compare the vocal style across non-ID coda types across clans and within the same clan. The results however are aggregated to highlight the differences in style between the clans and a a coda type-only comparison is not shown.
Comment 11
Lines 390-392: I’m assuming this is why pairwise comparisons were directional (i.e., there was both an A:B and a B:A comparison)? Can you speak to why A:B and B:A comparisons can have such different overlap values?
Given two clans—for example, the Four-Plus and the Short clan—spatial overlap is calculated twice: as the proportion of the Four-Plus clan’s repertoires that were recorded within 1,000 km of at least one of the Short clan’s repertoires, and as the proportion of the Short clan’s repertoires that were recorded within 1,000 km of at least one of the Four-Plus clan’s repertoires.
Order is important in these pairwise comparisons and generates an asymmetric matrix because the clans have different spatial extents. A clan found in only one small region might overlap completely with a clan that spans the Pacific Ocean, while the opposite is not true. For example, the Short clan spans the Pacific Ocean while the Four-Plus clan has been documented over a smaller area (but that smaller area overlaps extensively with the Short clan range). That is why the value is smaller (0.6) when considering how much of the Short clan’s range is shared with the Four-Plus clan, and larger (0.95) when considering how much of the Four-Plus clan’s range is shared with the Short clan.
Action - We now include the clan spatial overlap matrix as a supplemental table (Table S5).
Comment 13
Line 56: Can you briefly explain what memory means in the context of Markov chains?
We provide an explanation of the meaning of memory in the Methods section on ”Variable length Markov Chains”. Briefly, the memory in this case means how many states in the past of the Markov chain’s current state are required to predict the next transition of the chain itself. Standard Markov chains “look” back only one time step, while k-th order Markov chains look back k steps. In our case, there was no reason to assume that the memory required to predict different sequences of states (interclick intervals) should be the same across all sequences, and thus we adopted the formalism of variable length Markov chains, that allow for different levels of memory across the system.
Comment 14
Supplementary Figure S3: Like in the main manuscript, briefly explain or remind us what the blank nodes and the yellow nodes are.
Action - Clarified that the orange node represents the root of the tree in the figures.
Comment 15
Supplementary Figure S7: Put the letters before the dataset name.
Action - Done.
Comment 16
Supplementary Figure S10: Unclear what ’inner vs outer’ means.
One specifies comparisons across clans (outer) and the other within the same clan (inner)
Action - Added clarification on the caption of Figure S10
Comment 17
Supplementary Figure S14: Include a-c labels in the figure itself.
Action - Labels added to figure
Comment 18
Supplementary Figure S14: The information about the nodes is what needs to be included earlier and in the main body when discussing the trees.
Action - Added the explanation earlier in the text and in the main body
Reviewer #2 (Recommendations):
Comment 19
Line 22: ”Symbolic” and ”Arbitrary” are not synonyms. Please see the comment above.
We agree. Here, we make the point that the evolution of symbolic markers of group identity can be explained from what are initially arbitrary, and meaningless, signals (see [L1, L2]). Our point being that any vocalization, any coda, could have become selected for as an identity coda, and to become symbolic, and evolve to play a key role in cultural group formation and in-group favoritism because they enable a community of individuals to solve the problem of with whom to collaborate. The specific coda itself does not affect collaborative pay offs, but group specific differences in behavior can, as such the coda is arguably symbolic; as it is observable and recognizable, and can serve as a means for social assortment even when the behavioural differences are not. This can explain the means by which the social segregation which is observed among behaviorally distinct clans of sperm whales. However, in this manuscript, we do not extend this discussion of existing literature and have attempted to concisely describe this in a couple of lines, which clearly do a disservice to the large body of literature on the evolution of symbolic markers and human ethnic groups. We have added some citations to this section so that the reader may follow up should they disagree with out brief introductory statements.
Action - Added citations and pointers to the literature.
Comment 20
Line 24: The authors’ terminology around ”markers”, ”arbitrary”, ”symbolic” is unnecessarily confusing and mystifying, giving the impression these terms are interchangeable. They are not. These terms are an integral and long-established part of key definitions in signal theory. Term use should be followed accordingly. The observation that whale vocal signals vary per population does not necessarily mean that they function as a social tag. The word ”dog” varies per population but its use relates to an animal, not the population that utters the word. ”Dog” is not ”symbolic” of England, English-speaking populations or the English language. Furthermore, the function of whale vocal signals is extremely challenging to determine. In the best conditions, researchers can pin the signal’s context, this is distinct from signal’s function and further even for the signal’s meaning. How exactly the authors determine that whale vocal signals are arbitrary is, thus, perplexing given that this would require a detailed description and understanding of who is producing the song, when, towards whom, and how the receivers react, none of which the authors have and without which no claim on the signals’ function can be made. This terminological laxness and the sensu latu in extremis to various terms in an unjustified, unnecessary and unhelpful.
We use these terms as established in Hersh et al 2022 and the works leading up to it over the last 20 years in the study of sperm whales. These are often derived from definitions by Boyd and Richerson’s work on culture in humans and animals along with evolution of symbolic markers both in theory and in humans. We agree with the reviewer that these are difficult to establish in non-humans, whales or otherwise, but feel strongly that the accumulating evidence provides strong support for the function of these signals as symbolic markers of cultural groups, and that they likely evolved from initially arbitrary calls which were a part of the vocal repertoire (similar to the process and selective environment in Efferson et al. [L1] and McElreath et al. [L2]). We feel that we do not use these terms interchangeably here, and have inherited their use from definitions from anthropology. The work presented here uses terminology built across two decades of work in cetacean, and sperm whale, culture. And do not feel that these terms should be omitted here.
Comment 21
Lines 21-27: Overly broad and hazy paragraph.
We hope the replies above and our changes satisfy this comment and clarify the text.
Comment 22
Figure 1 legend: What are ”memory structures”? Unjustified descriptor.
The phrase was chosen to make draw some intuition on the variation of context length in variable length markov models.
Action - Re-worded from memory structures to statistical properties
Comment 23
Line 30: Omit ”finite”.
Action - Omitted.
Comment 24
Line 31: Please define and distinguish ”rhythm” and ”tempo”. Also see comment above, rhythm and tempo definitions require the use of IOIs.
We disagree with the reviewer’s claims here. In our research specifically, and for sperm whale research generally, coda inter-click intervals (ICIs) are calculated as the time between the start of the first click and the start of the subsequent click. This makes ICIs identical to inter-onset intervals (IOIs) under all definitions we are aware of. For example, Burchardt and Knornschild [L3] define IOIs as such: “In a sequence of acoustic signals, the time span between the start of an element and the next element, comprising the element duration and the following gap duration”. We now include a sentence making this point.
Regardless, we disagree on a more fundamental level with the statement that unless researchers quantify inter-onset intervals (IOIs), they cannot make any claims about rhythm. There are many studies that investigate rhythmic aspects of human and animal vocalizations without using IOIs [L4–L7]. If the duration of sound elements of interest is relatively constant (as is the case for sperm whale clicks), then rhythm analyses can still be meaningfully conducted on inter-call intervals (the silent intervals between calls).
For sperm whales, coda rhythm is defined by the relative ICIs standardized by their total duration. These can be clustered into discrete, defined rhythm types based on characteristic ICI patterns. Coda tempo is relative to the total duration of the coda itself. This can also be clustered into discrete tempo types across all coda durations as well (see [L8]).
Action - We added a sentence specifying that in this case we can use both ICIs and IOIs because of the standardized length of a single click.
Comment 25
Line 36: Are there non-vocalized codas to require the disambiguation here?
No, we have omitted for clarity.
Comment 26
Line 44: ”Higher” than which other social group class?
Sperm whales live in a multi-level social organization. Clans are a “higher” level of social organization than the social “units” which we define in line 40. Clans are made up of all units which share similar production repertoire of codas.
Action - We have added ’above social units’ on line 44 to make this clear.
Comment 27
Line 47: The use of “symbolic” continues to be enigmatic, even if authors are taking in this classification from other researchers. In signal theory (semiotics), not all biomarkers are necessarily symbols. I advise the authors to avoid the use of the term colloquially and instead adopt the definition used in the research field within which the study falls in.
There is ample examples of the use of ”symbolic” when referring to markers of in-group membership both in human and non-human cultures.Our choice to use the term “symbolic” is based on a previous study [L9] that found quantitative evidence that sperm whale identity codas function as symbolic markers of cultural identity, at least for Pacific Ocean clans. The full reasoning behind why the authors used the term “symbolic markers” is given in that paper, but briefly, they found evidence that identity coda usage becomes more distinct as clan overlap increases, while non-identity coda usage does not change. This matches theoretical and empirical work on human symbolic markers[L1, L2, L10, L11].
Action - We retain the use of the term here, as defined in the works cited, and based on its prior usage in the study of both human and non-human cultures.
Comment 28
Line 50: This statement is not technically accurate. The use of a signal as a marker by individuals can only be determined by how individuals ”interpret” and react to that signal - e.g., via playback experiments - it cannot be determined by how different populations use and produce the signals.
We respectfully disagree. While we agree that the optimal situation would be that of playback, the contextual use can provide insight into the functional use of signals; as can expected patterns of use and variation, as was tested in the papers we cite. However, this argument is not the scope nor the synthesis of this paper. These statements are supported by existing published works, as cited, and we encourage the reviewer to take exception with those papers.
Comment 29
Line 69: ”Meaningful speech characteristics”??? These terms do not logically or technically follow the previous statement. Why not stay faithful to the results and state that the method used seems to be valid and reliable because it confirms former studies and methods?
Action - Reworded to better underline the method’s results with previous studies
Comment 30
Lines 72-74: This statement doesn’t seem to accurately capture/explain/resume the difference between ID and non-ID codas.
We are not sure what the reviewer is referring to in this case. The sentence in this case was meant to explain the different relations that ID/non-ID codas have with clan sympatry.
Comment 31
Line 75: The information provided in the few previous sentences does not allow the reader to understand why these results support the notion that cultural transmission and social learning occurs between clans.
We conclude out introduction with a brief summary of our overall findings, which we then use the rest of the manuscript to support these statements.
Comment 32
Table 1: So far, the authors refer to their analyses as capturing the ”rhythm” of whale clicks. Consequently, it is not readily clear at this point why the authors rely on ”ICIs” (inter click intervals) instead of the ”universal” measure used across taxa to capture the rhythm of signal sequences - IOIs (inter onset intervals). If ICIs are the same measure as IOIs, why not use the common term, instead of creating a new term name? Alternatively, if ICIs are not equivalent to IOIs, then arguably the analyses do not capture the ”rhythm” of whale clicks, as claimed by the authors. Any rhythmic claim will need to be based on IOI measures. In animal behaviour, stereotyped is primarily used to describe pathological, dysfunctional behaviour. I suggest the use of other adjective, such as ”regular”, ”repetitive”, ”recurring”, ”predictable”. Another deviation from typical terminology: ”usage frequency” -¿ ”production rate”. Why is a clan a ”higher-order” level of social organization? This requires explanation, at least a mention, of what are the ”lower-order” levels. To the non-expert reader, there is a logical circularity/gap here: Clans are said to produce clan-specific codas, and then, it is said that codas are used to delineate clans. Either one deduces, or one infers, but not both. This raises the question, are clans confirmed by any other means than codas?
We are not creating a “new term name”: inter-click interval (ICI) is the standard terminology used in odontocete (toothed whale) research. We take the reviewer’s point that some readers will not be coming to our paper with that background, however, and now explicitly point out that ICI is synonymous with IOI for sperm whales. Please see our response to your earlier comment for more on this point.
Comment 33
Line 92: Unclear term, ”sub-sequence”. Fig. 1B doesn’t seem to readily help disambiguate the meaning of the term.
In fact reference to Fig. 1B is misplaced as it does not refer to the text. A sub-sequence is simply a contiguous subset of a coda, a subset of it.
Action - Removed ambiguous reference to Fig. 1B
Comment 34
Line 94: How does the use of ”sequence” compare here with ”sub-sequence” above?
In fact its the same situation although the previous comment highlighted a source of ambiguity.
Action - Reworded the sentence to be less confusing.
Comment 35
Line 95: Signal sequences don’t ”contain” memory, they require memory for processing.
Action - Rephrased from “sequences contain memory” to “states depend on previous sequences of varying length”.
Comment 36
Lines 95-97: The analogy with human language seems forced, combinatorics in any given species are expected to entail different transitions between unit/unit-sequences.
Thank you for the comment. Indeed, the purpose of the analogy is to illustrate how variable length Markov Chains work (which have been shown to be good at discerning even accents of the same language). We used human language as an analogy to provide the readers’ with a more intuitive understanding of the results.
Action - Revised paragraph to read: “Despite we do not have direct evidence of unitary blocks in sperm whale communication, on can imagine this effect similarly to what happens with words (e.g., a word beginning with “re” can continue in more ways than one starting with “zy”).”
Comment 37
Line 97: Unclear which possibility is this.
Action - Made the wording clearer.
Comment 38
Line 99: Invocation of memory, although common in the use of Markov chains, in inadequate here given that the research did not study how individuals perceived or processed click sequences, only how individual produced click sequences. If the authors are referring to the cognitive load imposed by producing clicks sequences, terms such as ”sequence planning” will be more accurate.
Here, we use the term “fixed-memory” in relation to the definition of a variable length Markov model. We feel that, in this section of the manuscript, the context is clear that it is a mathematical definition and in no way invokes the biological idea of memory or cognition. It is rather standard to use memory to describe the order of Markov chains. Swapping words in the definition of mathematical objects when the context is clear seems to cause unnecessary ambiguity.
Action - We clarified this in the manuscript (see comments above).
Reviewer #3 (Recommendations):
Comment 39
Line 16: Add ”broadly defined” as there are many other more restricted definitions (see for example Tomasello 1999; 2009). Tomasello M (1999) The cultural origins of human cognition. Harvard University Press, Cambridge Tomasello M (2009) The question of chimpanzee culture, plus postscript (chimpanzee culture 2009). In: Laland KN, Galef BG (eds) The question of animal culture. Harvard University Press, Cambridge, pp 198-221.
Thanks for the clarification.
Action - We added the term “broadly” and added the last reference.
Comment 40
Line 22: Is all stable social learned behavior that becomes idiosyncratic and ”distinguishable” considered symbolic markers? If not, consider adding ”potentially.”
No, but the evolution of cultural groups with differing behavior can reorganize the selective environment in such a way that it can favour an in-group bias that was not initially advantageous to individuals and lead to a preference towards others who share an overt symbolic marker that initially had no meaning and a random frequency in both populations. That is to say, even randomly assigned trivial groups can evolve arbitrary symbolic markers through in-group favouritism once behavioural differences exist even in the absence of any history of rivalry, conflict, or competition between groups. See for example [L1, L2].
Comment 41
Table 1: Identity codas are defined as a ”Subset of coda types most frequently used by a sperm whale clan; canonically used to define vocal clans.” Therefore, I infer that an identity coda is not exclusively used by a specific clan and may be utilized by other clans, albeit less frequently. If this is the case, what criteria determine the frequency of usage for a coda to be categorized as an identity or non-identity coda? Does the criteria used to differentiate between ID and non-ID codas reflect the observed differences in micro changes between the two and within clans?
The methods for this categorization are defined, discussed, and justified in previous work in [L9, L12]. We feel its outside the scope of this paper to review these details here in this manuscript. However, the differences between vocal styles discussed here and the frequency production repertoires which allow for the definition of identity codas are on different scales. The differences between identity and non-identity codas are not the observed differences in vocal style reported here.
Comment 42
Table 1: The definition of vocal style states that it ”Encodes the rhythmic variations within codas.” However, if rhythm changes, does the type of coda change as well? Typically, in musical terms, the component that maintains the structure of a rhythm is ”tempo,” not ”rhythm.” How much microvariation is acceptable to maintain the same rhythm, and when do these variations constitute a new rhythm?
Thank you for raising this important point about the relationship between rhythmic variations and coda categorization. In our definition, ”vocal style” refers to subtle, micro-level variations in the rhythmic structure of codas that do not alter their overarching categorical identity. These microvariations are akin to ”tempo” changes in musical terms, which can modify the expression of a rhythm without fundamentally altering its structure.
The threshold at which microvariations constitute a new rhythm, and thus a new coda type, remains an open question and is a limitation of current analytical approaches. In our study, we used established classification methods to group codas into types, treating variations within these groups as part of the same rhythm. Future work could refine these thresholds to better distinguish between meaningful rhythmic variation and the emergence of new coda types.
Comment 43
Table 1: Change ”say” to ”vocalize” (similarly as used in line 273 for humpback whales ”vocalizations”).
Thanks.
Action - Done.
Comment 44
Lines 33-35 and Figure 1-C: Can a lay listener discern the microvariations within each coda type by ear? Consider including sound samples of individual rhythmic microvariations for the same coda type pattern (e.g., Four plus, Palindrome, Plus One, Regular) to provide readers/listeners with an impression of their detectability. If authors considered too much or redundant Supplemental material at least give a sound sample for each the 4 subcodas modeled structures examples of 4R2 coda variations depicted in Figure 1-C so the reader can have an acoustic impression of them.
We do not think that human listeners would be able to all of the variation detected here. However, this does not mean that it is not important variation for the whales. Human observers being able to classify call variation aurally shouldn’t be seen as a bar representing important biological variation for non-human species, given that their hearing and vocal production systems have evolved independently. Importantly, ’Four Plus’,’Palindrome’, etc are names of Clans; sympatric, but socially segregated, communities of whale families, which share a distinct vocal dialect of coda types. These clans each have have distinguishable coda dialects made up of dozens of coda types (and delineated based on identity codas), these are not names/categorical coda types themselves.
Action - We now provide audio samples of all coda types listed in Figure 1B in the paper’s Github repository.
Comment 45
Line 69: As stated above, it may be confusing to refer to it as ”speech.” I suggest adding something like: ”Our method does capture one essential characteristic of human speech: phonology.” Reply 45.—Thank you for drawing our attention to this.
Action - We removed the word “speech” from the manuscript, using “communication” and/or “vocalization” depending on the context.
Comment 46
Line 111-112: Consider adding a sound sample of the variation of the 4R2 coda type that can be vocalized as BCC but also as CBB as supplementary data.
What the reviewer has correctly observed is that the traditional categorical coda type ’names’ do not capture the variation within a type by rhythm nor by tempo.
Action - We have added samples of all coda types listed in Figure 1B in the paper’s Github repo.
Comment 47
Figure 3: Include a sound sample for each of the 7 coda types in Figure 1B (”specific vocal repertoires”) to illustrate the set of coda types used and their associated usage frequencies, or at least for each of the 7 coda types in Figure 3 and tables S1 and S2.
Sperm whales in the Eastern Caribbean produce dozens of rhythm types across at least five categorical tempo types [L8, L13]. The coda types represented in Figure 1B do not demonstrate all the variability inherent in the sperm whales’ vocal dialect. Importantly, Figure 3, as well as table S1 and S2, refer to clan-level dialects not specific individual coda types.
Action - We added sound samples for each coda rhythm type listed in Figure 1B to the Github repository.
Comment 48
Lines 184-190: It is unclear what human analogy term is used for ID codas. This needs clarification.
We are not making an analogy in humans for the role of ID vs non-ID codas, but only providing the example of accents as changes in vocalization (style) without a change in the actual words used (repertoire).
Action - We tried to make it clearer in the manuscript.
Comment 49
Line 190: Change ”whale speech” to ”whale vocalizations.”
Thanks.
Action - Done.
Comment 50
Figure 4: Correct citation number Hersh ”10” to Hersh ”11.”
Thanks.
Action - Fixed the reference.
Comment 51
Lines 224-232: Clarify whether the reference to how spatial overlap affects the frequency of ID codas refers to shared ID codas between clans or the production frequency of each coda within the total repertoire of codas.
The similarity between ID coda repertoires we are referring to there is based on the ID codas of both clans.
More details on the comparison can be found in [L9].
Action - We added a sentence explaining the comparison is made using the joint set of ID codas.
Comment 52
Lines 240-241: What are non-ID codas vocal cues for?
Non-ID codas likely serve as flexible, context-dependent signals that facilitate group coordination, convey environmental or social context, and promote social learning, especially in mixed-clan or overlapping habitats. Their variability suggests multifunctional roles shaped by ecological and social pressures.
Comment 53
Lines 267-268: It’s unclear whether non-ID coda vocal styles are genetically inherited or not, as argued in lines 257-258.
We did not intend to argue that non-ID coda vocal styles are genetically inherited. Instead, we aimed to present a hypothetical consideration: if non-ID coda vocal styles were genetically inherited, one would expect a direct correlation between vocal style similarity and genetic relatedness. This hypothetical framework was introduced to strengthen our argument that the observed patterns are unlikely to be explained by genetic inheritance, as such correlations have not been observed. While we acknowledge that we lack definitive proof to rule out genetic influences entirely, the evidence available strongly suggests that social learning, rather than genetic transmission, is the more plausible mechanism.
Action - Clarified in manuscript.
Comment 54
Line 277: Can males mate with females from different clans?
Yes, genetic evidence shows that males may even switch ocean basins.
Action - We have clarified that we mean the female members of units from different clans have only rarely been observed to interact at sea between clans.
Comment 55
Lines 287-292: Consider discussing the difference between controlled/voluntary and automatic/involuntary imitation and their implications for cultural selection and social learning (see Heyes 2011; 2012). Heyes, C. (2011). Automatic imitation. Psychological bulletin, 137(3), 463. Heyes, C. (2012). What’s social about social learning?. Journal of comparative psychology, 126(2), 193.
Thank you for your insightful comment regarding this. The distinction between controlled/voluntary and automatic/involuntary imitation, as highlighted by Heyes [L14, L15], provides a potentially valuable framework for interpreting social learning mechanisms in sperm whales. Automatic imitation refers to reflexive, often unconscious mimicry driven by perceptual or motor coupling, while controlled imitation involves deliberate and goal-directed efforts to replicate behaviors. Both forms likely play complementary roles in the cultural transmission observed in sperm whales.
This dual-process perspective highlights the potential for cultural selection to act at different levels. Automatic imitation may drive convergence in shared environments, promoting acoustic homogeneity and facilitating inter-clan communication. In contrast, controlled imitation ensures the preservation of clan-specific vocal traditions, maintaining cultural diversity. This interplay between automatic and controlled processes could reflect a balancing act between cultural assimilation and differentiation, underscoring the adaptive value of these mechanisms in dynamic social and ecological contexts.
Action - We have incorporated a short discussion of this distinction and its implications for our findings in the Discussion. Additionally, we have cited [L14, L15] to provide theoretical grounding for this interpretation.
Comment 56
Methods: Consider integrating the paragraph from lines 319-321 into lines 28-35 and eliminate redundant information.
Thanks.
Action - We implemented the suggestion, removing the first paragraph of the Dataset description and integrating the information when we introduce the concepts of codas and clicks.
[L1] C. Efferson, R. Lalive, and E. Fehr, Science 321, 1844 (2008).
[L2] R. McElreath, R. Boyd, and P. Richerson, Curr. Anthropol. 44, 122 (2003).
[L3] L. S. Burchardt and M. Knornschild, PLoS Computational Biology 16, e1007755 (2020).
[L4] A. Ravignani and K. de Reus, Evolutionary Bioinformatics 15, 1176934318823558 (2019).
[L5] C. T. Kello, S. D. Bella, B. Med´ e, and R. Balasubramaniam, Journal of the Royal Society Interface 14, 20170231 (2017).
[L6] D. Gerhard, Canadian Acoustics 31, 22 (2003).
[L7] N. Mathevon, C. Casey, C. Reichmuth, and I. Charrier, Current Biology 27, 2352 (2017).
[L8] P. Sharma, S. Gero, R. Payne, D. F. Gruber, D. Rus, A. Torralba, and J. Andreas, Nature Communications 15, 3617 (2024).
[L9] T. A. Hersh, S. Gero, L. Rendell, M. Cantor, L. Weilgart, M. Amano, S. M. Dawson, E. Slooten, C. M. Johnson, I. Kerr, et al., Proc. Natl. Acad. Sci. 119, e2201692119 (2022).
[L10] R. Boyd and P. J. Richerson, Cult Anthropol 2, 65 (1987). [L11] E. Cohen, Curr. Anthropol. 53, 588 (2012).
[L12] T. A. Hersh, S. Gero, L. Rendell, and H. Whitehead, Methods Ecol. Evol. 12, 1668 (2021), ISSN 2041-210X, 2041-210X.
[L13] S. Gero, A. Bøttcher, H. Whitehead, and P. T. Madsen, R. Soc. Open Sci. 3, 160061 (2016).
[L14] C. Heyes, Psychological Bulletin 137, 463 (2011).
[L15] C. Heyes, Journal of Comparative Psychology 126, 193 (2012).
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Reviewer #1 Evidence, reproducibility and clarity Summary: Bhatt et al. seek to define factors that influence H3.3 incorporation in the embryo. They test various hypotheses, pinpointing the nuclear/cytoplasmic ratio and Chk1, which affects cell cycle state, as influencers. The authors use a variety of clever Drosophila genetic manipulations in this comprehensive study. The data are presented well and conclusions reasonably drawn and not overblown. I have only minor comments to improve readability and clarity. I suggest two OPTIONAL experiments below. We thank the reviewer for their positive and helpful comments. Major comments: We found this manuscript well written and experimentally thorough, and the data are meticulously presented. We have one modification that we feel is essential to reader understanding and one experimental concern: The authors provide the photobleaching details in the methodology, but given how integral this measurement is to the conclusions of the paper, we feel that this should be addressed in clear prose in the body of the text. The authors explain briefly how nuclear export is assayed, but not import (line 99). Would help tremendously to clarify the methods here. This is especially important as import is again measured in Fig 4. This should also be clarified (also in the main body and not solely in the methods). We have added the following sentences to the main body of the text to clarify how photobleaching and import were assayed. “We note that these differences are not due to photobleaching as our measurements on imaged and unimaged embryos indicate that photobleaching is negligible under our experimental conditions (see methods, Figure S1G-H)” lines 98-101 and “Since nuclear export is effectively zero, we attribute the increase in total H3.3 over time solely to import and therefore the slope of total H3.3 over time corresponds to the import rate.” lines 111-113 Revision Plan In addition we have clarified how import was calculated to figure legends in Figure 5D (formerly 4D) and S1F which now read: “Initial slopes of nuclear import curves (change in total nuclear intensity over time for the first 5 timepoints) …” We also added the following explanation of how nuclear import rates were calculated to the methods section: “Import rates were calculated by using a linear regression for the total nuclear intensity over time for the first 5 timepoints in the nuclear import curves.” lines 471-473, methods If the embryos appeared "reasonably healthy" (line 113) after slbp RNAi, how do the authors know that the RNAi was effective, especially in THESE embryos, given siblings had clear and drastic phenotype? This is especially critical given that the authors find no effect on H3.3 incorporation after slbp RNAi (and presumably H3 reduction), but this result would also be observed if the slbp RNAi was just not effective in these embryos. We apologize for the confusion caused by our word choice. The “healthy” slbp-RNAi embryos had measurable phenotypes consistent with histone depletion that we have reported previously (Chari et al, 2019) including cell cycle elongation and early cell cycle arrest (Figure S4D). However, they did not have the catastrophic mitosis observed in more severely affected embryos. We agree with the reviewer that a concern of this experiment is that the less severely affected embryos likely have more remaining RD histones including H3. To address this we also tested H3.3 incorporation in the embryos that fail to progress to later cell cycles in the cycles that we could measure. Even in these more severely affected embryos we were not able to detect a change in H3.3 incorporation relative to controls (lines 240-243 and Fig S4B). Unfortunately, it is impossible to conduct the ideal experiment, which would be a complete removal of H3 since this is incompatible with oogenesis and embryo survival. To address this confusion we have added supplemental videos of control, moderately affected and severely affected SLBP-RNAi embryos as movies 3-5 and modified the text to read: “All embryos that survive through at least NC12, had elongated cell cycles in NC12 and 60% arrested in NC13 as reported previously indicating the effectiveness of the knockdown (Figure S4C, Movie 3-5)39. In these embryos, H3.3 incorporation is largely unaffected by the reduction in RD H3 (Figure 6B).” lines 236-240 Finally, to characterize the range of SLBP knockdown in the RNAi embryos we propose to do single embryo RT-qPCRs for SLBP mRNA for multiple individual embryos. This will provide a measure of the range knockdown that we observed in our H3.3 movies. Minor comments: Introduction: Revision Plan Consider using "replication dependent" (RD) rather than "replication coupled." Both are used in the field, but RD parallels RI ("replication independent"). We thank the reviewer for this suggestion. We have made the text edits to change "replication coupled" (RC) to "replication dependent" (RD) throughout the manuscript. Would help for clarity if the authors noted that H3 is equivalent to H3.2 in Drosophila. Also it is relevant that there are two H3.3 loci as the authors knock mutations into the H3.3A locus, but leave the H3.3B locus intact. The authors should clarify that there are two H3.3 genes in the Drosophila genome. We have changed the text as follows to increase clarity as suggested: “Similarly, we have previously shown that RD H3.2 (hereafter referred to as H3) is replaced by RI H3.3 during these same cycles, though the cause remains unclear29” lines 52-54 “There are ~100 copies of H3 in the Drosophila genome, but only 2 of H3.3 (H3.3A and H3.3B)26. To determine which factor controls nuclear availability and chromatin incorporation, we genetically engineered flies to express Dendra2-tagged H3/H3.3 chimeras at the endogenous H3.3A locus, keeping the H3.3B locus intact.” lines 127-131 Please add information and citation (line 58): H3.3 is required to complete development when H3.2 copy number is reduced (PMID: 37279945, McPherson et al. 2023) We have added the suggested information. The text now reads “Nonetheless, H3.3 is required to complete development when H3.2 copy number is reduced54.” lines 61-62 Results: Embryo genotype is unclear (line 147): Hira[ssm] haploid embryos inherit the Hira mutation maternally? Are Hira homozygous mothers crossed to homozygous fathers to generate these embryos, or are mothers heterozygous? This detail should be in the main text for clarity. The Hira mutants are maternal effect. We crossed homozygous Hirassm females to their hemizygous Hirassm or FM7C brothers. However, the genotype of the male is irrelevant since the Hira phenotype prevents sperm pronuclear fusion and therefore there is no paternal contribution to the embryonic genotype. We have clarified this point in the text: “We generated embryos lacking functional maternal Hira using Hirassm-185b (hereafter Hirassm) homozygous mothers which have a point mutation in the Hira locus57.” lines 160-162 Revision Plan Line 161: Shkl affects nuclear density, but it also appears from Fig 3 to affect nuclear size? The authors do not address this, but it should at least be mentioned. We thank the reviewer for the astute observation. More dense regions of the Shkl embryos do in fact have smaller nuclei. We believe that this is a direct result of the increased N/C ratio since nuclear size also falls during normal development as the N/C ratio increases. We have added a new figure 1 in which we more carefully describe the events of early embryogenesis in flies including a quantification of nuclear size and number in the pre-ZGA cell cycles (Figure 1C). We also note the correlation of nuclear size with nuclear density in the text: “During the pre-ZGA cycles (NC10-13), the maximum volume that each nucleus attains decreases in response to the doubling number of nuclei with each division (Figure 1C).” lines 86-87 “To test this, we employed mutants in the gene Shackleton (shkl) whose embryos have non-uniform nuclear densities and therefore a gradient of nuclear sizes across the anterior/posterior axis (Figure 3A-B, Movie 1-2)58.” lines 180-183 The authors often describe nuclear H3/H3.3 as chromatin incorporated, but these image-based methods do not distinguish between chromatin-incorporated and nuclear protein. To distinguish between chromatin incorporated and nuclear free histone we have exploited the fact that histones that are not incorporated into DNA freely diffuse away from the chromatin mass during mitosis while those that are bound into nucleosomes remain on chromatin during this time. In our previous study we showed that H3-Dendra2 that is photoconverted during mitosis remains stably associated with the mitotic chromatin through multiple cell cycles (Shindo and Amodeo, 2019) strengthening our use of this metric. To help clarify this point as well as other methodological details we have added a new Figure 1B which documents the time points at which we make various measurements within the lifecycle of the nucleus. We also edited the text to read: “We have previously shown that with each NC, the pool of free H3 in the nucleus is depleted and its levels on chromatin during mitosis decrease (Figure 1D, S1C-D)29. In contrast, H3.3 mitotic chromatin levels increase during the same cycles (Figure 1D, S1C-D)29.” lines 89-92 I very much appreciate how the authors laid out their model in Fig 3 and then used the same figure to explain which part of the model they are testing in Figs 4 and 5. This is not a critique- we can complement too! Thank you! Revision Plan OPTIONAL experimental suggestion: The experiments in Figure 4 and 5 are clever. One would expect that H3 levels might exhaust faster in embryos lacking all H3.2 histone genes (Gunesdogan, 2010, PMID: 20814422), allowing a comparison testing the H3 availability > H3.3 incorporation portion of the hypothesis without manipulating the N/C ratio. This might also result in a more consistent system than slbp RNAi (below). We thank the reviewer for the experimental suggestion. We also considered this experimental manipulation to decrease RD histone H3.2. We chose not to do this experiment because in the Gunesdogan paper they show that the zygotic HisC nulls have normal development until after NC14 (unlike the maternal SLBP-RNAi that we used) suggesting that maternal H3.2 supplies do not become limiting until after the stages under consideration in our paper. Maternal HisC-nulls are, of course, impossible to generate since histones are essential. O'Haren 2024 (PMID: 39661467) did not find increased Pol II at the HLB after zelda RNAi (line 227). Might also want to mention here that zelda RNAi does not result in changes to H3 at the mRNA level (O'Haren 2024), as that would confound the model. We thank the reviewer for the suggestion. We have removed the discussion of Pol II localization and replaced it with the information about histone mRNA : “zelda controls the transcription of the majority of Pol II genes during ZGA but disruption of zelda does not change RD histone mRNA levels67–70”. lines 249-251 Discussion: Should discuss results in context of McPherson et al. 2023 (PMID: 37279945), who showed that decreasing H3.2 gene numbers does not increase H3.3 production at the mRNA or protein levels. We expanded our discussion to include the following: “Given the fact that H3.3 pool size does not respond to H3 copy number in other Drosophila tissues,54 our results suggest that H3.3 incorporation dynamics are likely independent of H3 availability.” lines 278-280 The Shackleton mutation is a clever way to alter N/C ratio, but the authors should point out that it is difficult (impossible?) to directly and cleanly manipulate the N/C ratio. For example, Shkl mutants seem to also have various nuclear sizes. As discussed above, we think that nuclear size is a direct response to the N/C ratio. We have added the following sentence to the discussion as well as a citation to a paper which discusses how the N/C ratio might contribute to nuclear import in early embryos to the discussion: “This may be due to N/C ratio-dependent changes in nuclear import dynamics which may also contribute to the observed changes in nuclear size across the shkl embryo75.” lines 307-309 Revision Plan How is H3.3 expression controlled? Is it possible that H3.3 biosynthesis is affected in Chk1 mutants? To address this question we propose to perform RT-qPCR for H3.3A and H3.3B as well as Hira in the Chk1 mutant. Unfortunately, we do not have antibodies that reliably distinguish between H3 and H3.3 in our hands (despite literature reports), but we will also perform a pan-H3 immunostaining in the Chk1 embryos to measure how the total H3-type histone pool changes as a result of the loss of Chk1. Figures: While I appreciate the statistical summaries in tables, it is still helpful to display standard significance on the figures themselves. We have added statistical comparisons in Figure 3 (formerly Figure 2). We do not feel that it is appropriate to directly compare the intensities of the H3-Dendra2 construct expressed from the pseudo-endogenous locus to the H3.3 and chimeric proteins expressed from the H3.3A locus as they were imaged using different settings. Although we plot H3 on the same graph as the other proteins to allow for ease of comparison of their trends over time it is not appropriate to directly compare their normalized intensities which including statistical tests would encourage. We have added a note to the legend of Figure 1 explaining this which reads: “Note that statistical comparisons between the two Dendra2 constructs have not been done as they were expressed from different loci and imaged under different experimental settings.” Fig 1: A: Is it possible to label panels with the nuclear cycle? We have done this. B: Statistics required - caption suggests statistics are in Table S2, but why not put on graph? Please see the explanation above for why we do not feel that it is appropriate to perform this comparison. C/D: Would be helpful if authors could plot H3/H3.3 on same graph because what we really need to compare is NC13 between H3/H3.3 (and statistics between these curves) Please see the explanation above for why we do not feel that it is appropriate to perform this comparison. These curves can be directly compared within a construct and we can evaluate their trends over time, but the normalized values should not be directly compared in the way that would be encouraged by plotting the data as suggested. E: The comparison in the text is between H3.3 and H3, but only H3.3 data is shown. I realize that it is published prior, but the comparison in figure would be helpful. We have added the previously published values to the text. Revision Plan “These changes in nuclear import and incorporation result in a less complete loss of the free nuclear H3.3 pool (~70% free in NC11 to ~30% in NC13) than previously seen for H3 (~55% free in NC11 to ~20% in NC13)” lines 116-119 Fig 2: A: A very helpful figure. Slightly unclear that the H3 that is not Dendra tagged is at the H3.3 locus. Also unclear that the H3.3A-Dendra2 line exists and used as control, as is not shown in figure. Should show H3 and H3.3 controls (Figure S2) We have edited the figure to add Dendra2 to all of the constructs and made clear the location of each construct including adding the landing site for H3-Dendra2. We have also cited Figure S1 in the legend which contains a more detailed diagram of the integration strategy. F/H- As the comparison is between H3 and ASVM, it would help to combine these data onto the same graph. As the color is currently used unnecessarily to represent nuclear cycle, the authors could use their purple/pink color coding to represent H3/ASVM. We have combined these data onto a single graph as requested and changed the colors appropriately. We have not added statistical comparisons to this graph as we again believe that they would be inappropriate. In the legend of Fig 2 the authors write "in the absence of Hira." Technically, there is only a point mutation in Hira. It is not absent. Good catch! We have changed this to “in Hirassm mutants”. Fig 3: G: Please show WT for comparison. Can use data in Fig 3A. We have added the color-coded number of neighbor embryo representations for WT and Shkl embryos underneath the example embryo images in 4A-B (formerly 3A-B,G). Model in H is very helpful (complement)! Thank you. Fig 4: B/C/F/G: The authors use a point size scale to represent the number of nuclei, but the graphs are so overlaid that it is not particularly useful. Is there a better way to display this dimension? We chose to represent the data in this way so that the visual impact of each line is representative of the amount of data (number of nuclei in each bin) that underlies it. This helps to prevent sparsely populated outlier bins at the edges of the distribution from dominating the interpretation of the data. If the reviewer has a suggestion for a better way to visualize this information we would welcome their suggestion, but we cannot think of a better way at this time. D/E/H/I: What does "min volume" mean on the X axis? Since the uneven N/C ratio in the shkl embryos results in a wavy cell cycle pattern there is no single time point where we can calculate the number of neighbors for the whole embryo (since Revision Plan not all nuclei are in the same cell cycle at a given point). Therefore, we had to choose a criterion for when we would calculate the number of neighbors for each nucleus. We chose nuclear size as a proxy for nuclear age since nuclear size increases throughout interphase (see new figure 1B). So, the minimum volume is the newly formed nucleus in a given cell cycle. We also tested other timepoints for the number of neighbors (maximum nuclear volume, just before nuclear envelope breakdown and midway between these two points) and found similar results. We chose to use minimum volume in this paper because this is the time point when the nucleus is growing most quickly and nuclear import is at its highest. We have added the following explanation to the methods: “For shkl embryos, as the nuclear cycles are asynchronous, nuclear divisions start at different timepoints within the same cell cycle and the nuclear density changes as the neighboring nuclei divide. Therefore, the total intensity traces were aligned to match their minimum volumes (as shown in Figure 1B) to T0.” lines 485-488, methods And the following detail to the figure legend: “...plotted by the number of nuclear neighbors at their minimum nuclear volume…” Figure 5 legend We also added a depiction of the lifecycle of the nucleus in which we marked the minimum volume as the new Figure 1B. Fig 5: F: OPTIONAL Experimental request: Here I would like to see H3 as a control. This is a very good suggestion, and we are currently imaging H3-Dendra2 in the Chk1 background. However, our preliminary results suggest that there may be some synthetic early lethality between the tagged H3-Dendra2 and Chk1 since these embryos are much less healthy than H3.3-Dendra2 Chk1 embryos or Chk1 with other reporters. In addition, we have observed a much higher level of background fluorescence in this cross than in the H3-Dendra2 control. We are uncertain if we will be able to obtain usable data from this experiment, but will continue to try to find conditions that allow us to analyze this data. As an orthogonal approach to answer the question, we will perform immunostaining with a pan-H3 antibody in Chk1 mutant embryos to measure total H3 levels under these conditions. Since the majority of H3-type histone is H3.2 and we know how H3.3 changes, this staining will give us insight into the dynamics of H3 in Chk1 mutant embryos. Significance General assessment: Many long-standing mysteries surround zygotic genome activation, and here the authors tackle one: what are the signals to remodel the zygotic chromatin around ZGA? This is a tricky question to answer, as basically all manipulations done to the embryo Revision Plan have widespread effects on gene expression in general, confounding any conclusions. The authors use clever novel techniques to address the question. Using photoconvertible H3 and H3.3, they can compare the nuclear dynamics of these proteins after embryo manipulation. Their model is thorough and they address most aspects of it. The hurdle this study struggles to overcome is the same that all ZGA studies have, which is that manipulation of the embryo causes cascading disasters (for example, one cannot manipulate the nuclear:cytoplasmic ratio without also altering cell cycle timing), so it's challenging to attribute molecular phenotypes to a single cause. This doesn't diminish the utility of the study. Advance: The conceptual advance of this study is that it implicates the nuclear:cytoplasmic ratio and Chk1 in H3.3 incorporation. The authors suggest these factors influence cell cycle closing, which then affects H3.3 incorporation, although directly testing the granularity of this model is beyond the scope of the study. The authors also provide technical advancement in their use of measuring histone dynamics and using changes in the dynamics upon treatment as a useful readout. I envision this strategy (and the dendra transgenes) to be broadly useful in the cell cycle and developmental fields. Audience: The basic research presented in this study will likely attract colleagues from the cell cycle and embryogenesis fields. It has broader implications beyond Drosophila and even zygotic genome activation. This reviewer's expertise: Chromatin, Drosophila, Gene Regulation Reviewer #2 (Evidence, reproducibility and clarity (Required)): This manuscript investigates the regulation of H3.3 incorporation during zygotic genome activation (ZGA) in Drosophila, proposing that the nuclear-to-cytoplasmic (N/C) ratio plays a central role in this process. While the study is conceptually interesting, several concerns arise regarding the lack of proper control experiments and the clarity of the writing. The manuscript is difficult to follow due to vague descriptions, insufficient distinctions between established knowledge and novel findings, and a lack of rigorous statistical analyses. These issues need to be addressed before the study can be considered for publication. We thank the reviewers for their careful reading of this manuscript. We have sought to clarify the concerns regarding clarity through numerous text edits detailed below. We did include ANOVA analysis for all of the relevant statistical comparisons in the supplemental table. However, to increase clarity we have also added some statistical comparisons in the main figures. We note that we do not feel that it is appropriate to directly compare the intensities of the H3-Dendra2 construct expressed from the pseudo-endogenous locus to the H3.3 and chimeric proteins expressed from the H3.3A locus as they were imaged using different settings. Although we plot H3 on the same graph as the other proteins to allow for ease of comparison of their trends over time it is not appropriate to directly compare their normalized intensities which including statistical tests would encourage. We have added a note to the legend of the new Figure 1 Revision Plan explaining this which reads: “Note that statistical comparisons between the two Dendra2 constructs have not been done as they were expressed from different loci and imaged under different experimental settings.” Major Concerns The manuscript would benefit from a clearer introduction that explicitly distinguishes between previously known mechanisms of histone regulation during ZGA and the novel contributions of this study. Currently, the introduction lacks sufficient background on early embryonic chromatin regulation, making it difficult for readers unfamiliar with the field to grasp the significance of the findings. The authors should also be more precise when discussing the timing of ZGA. While they state that ZGA occurs after 13 nuclear divisions, it is well established that a minor wave of ZGA begins at nuclear cycle 7-8, whereas the major wave occurs after cycle 13. Clarifying this distinction will improve the manuscript's accessibility to a broader audience. We have added a new figure 1 to make the timing and nuclear behaviors of the embryo during ZGA in Drosophila more clear. We have also added information about how the chromatin changes during Drosophila ZGA in the following sentence: “ In Drosophila, these changes include refinement of nucleosomal positioning, partitioning of euchromatin and heterochromatin and formation of topologically associated domains20–22,24.” lines 39-41 We have clarified the major and minor waves of ZGA in the introduction and results by adding the following sentences to the introduction and results respectively: “In most organisms ZGA happens in multiple waves but the chromatin undergoes extensive remodeling to facilitate bulk transcription during the major wave of ZGA (hereafter referred to as ZGA)18–20,22–25..” lines 36-39 “In Drosophila, ZGA occurs in 2 waves. The minor wave starts as early as the 7th cycle, while major ZGA occurs after 13 rapid syncytial nuclear cycles (NCs) and is accompanied by cell cycle slowing and cellularization (Figure 1A-B).” lines 83-85 We hope that these changes help to reduce confusion and make the paper more accessible. However, we are happy to add additional information if the reviewer can provide specific points which require further attention. One of the primary weaknesses of this study is the lack of adequate control experiments. In Figure 1, the authors suggest that the levels of H3 and H3.3 are influenced by the N/C ratio, but Revision Plan it is unclear whether transcription itself plays a role in these dynamics. To properly test this, RNA-seq or Western blot analyses should be performed at nuclear cycles 10 and 13-14 to compare the levels of newly transcribed H3 or H3.3 against maternally supplied histones. Without such data, the authors cannot rule out transcriptional regulation as a contributing factor. In the pre-ZGA cell cycles the vast majority of protein including histones is maternally loaded. Gunesdogan et al. (2010) showed that the zygotic RD histone cluster nulls survive past NC14 (well past ZGA) with no discernible defects indicating that maternal RD histone supplies are sufficient for normal development during the cell cycles under consideration. Therefore, new transcription of replication coupled histones is not needed for apparently normal development during this period. Moreover, we have done the western blot analysis using a Pan-H3 antibody as suggested by the reviewer in our previously published paper (Shindo and Amodeo, 2019 supplemental figure S3A-B) and found that total H3-type histone proteins only increase moderately during this period of development, nowhere near the rate of the nuclear doublings. We have added the following sentence to clarify this point. “These divisions are driven by maternally provided components and the total amount of H3 type histones do not keep up with the pace of new DNA produced29.” lines 88-89 We have also previously done RNA-seq on wild-type embryos (and those with altered maternal histone levels) (Chari et al 2019). In this RNA-seq (like most RNA-seq in flies) we used poly-A selection and therefore cannot detect the RD histone mRNAs (which have a stem-loop instead of a poly-A tail). We have plotted the mRNA concentrations for both H3.3 variants from that dataset below for the reviewers reference (we have not included this in the revised manuscript). The total H3.3 mRNA levels are nearly constant from egg laying (NC0- these are from unfertilized embryos) until after ZGA (NC14). These data combined with the westerns discussed above give us confidence that what we are observing is the partitioning of large pools of maternally provided histones with only a relatively small contribution of new histone synthesis. Revision Plan In Figure 2, the manuscript introduces chimeric embryos expressing modified histone variants, but their developmental viability is not addressed. It is essential to determine whether these embryos survive and whether they exhibit any phenotypic consequences such as altered hatching rates, defects in nuclear division, or developmental arrest. Tagging histones is often deleterious to organismal health. In Drosophila there are two H3.3 loci (H3.3A and H3.3B). In all of our chimera experiments we have left the H3.3B and one copy of the H3.3A locus unperturbed to provide a supply of untagged H3.3. This allows us to study H3.3 and chimera dynamics without compromising organism health. All of our chimeras are viable and fertile with no obvious morphological defects. We have added the following sentences to the text to clarify this point: “There are ~100 copies of H3 in the Drosophila genome, but only 2 of H3.3 (H3.3A and H3.3B)26. To determine which factor controls nuclear availability and chromatin incorporation, we genetically engineered flies to express Dendra2-tagged H3/H3.3 chimeras at the endogenous H3.3A locus, keeping the H3.3B locus intact….These chimeras were all viable and fertile. ” lines 127-131, 136 In addition we propose performing hatch rate assays for embryos from the chimeric embryos of S31A, SVM and ASVM to assess if there is any decrease in fecundity due to the presence of the chimeras. Moreover, given that H3.3 is associated with actively transcribed genes, an RNA-seq analysis of chimeric embryos should be included to assess transcriptional changes linked to H3.3 incorporation. This is an excellent suggestion and will definitely be a future project for the lab. However, to do this experiment correctly we will need to generate untagged chimeric lines that will (hopefully) allow for the full replacement of H3.3 with the chimeric histones instead of a single copy among 4. This is beyond the scope of this paper. Figures 3 and 4 raise additional concerns about whether histone cluster transcription is altered in shkl mutant embryos. The authors propose that the shkl mutation affects the N/C ratio, yet it remains unclear whether this leads to changes in the transcription of histone clusters. Furthermore, since HIRA is a key chaperone for H3.3, it would be important to assess whether its levels or function are compromised in shkl mutants. To address these gaps, RT-qPCR or RNA-seq should be performed to quantify histone cluster transcription, and Western blot analysis should be used to determine if HIRA protein levels are affected. The changes in the N/C ratio that are observed in the shkl mutant are within SINGLE embryo (differences in nuclear spacing). In these experiments we are comparing nuclei within a common cytoplasm that have different local nuclear densities (N/C ratios). Therefore, if Shkl Revision Plan were somehow affecting the transcription of histones or their chaperones we would expect all of the nuclei within the same mutant embryo to be equally affected since they are genetically identical and share a common cytoplasm. We do not directly compare the behavior of shkl embryos to wildtype except to demonstrate that there is no positional effect on the import of H3 and H3.3 across the length of the embryo in wildtype. To clarify our experimental system for these experiments we have added additional panels to Figure 4A and B that depict the number of neighbors for both control and Shkl embryos. Nonetheless, to address the reviewer’s concern that shkl may change the amount of H3 present in the embryo, we propose to conduct a western blot comparison of wildtype and shkl embryos using a pan-H3 antibody. There are no tools (antibodies or fluorescently tagged proteins) to assess HIRA protein levels in Drosophila. We therefore propose to perform RT-qPCR for HIRA in wildtype and shkl embryos. A similar issue arises in Figure 5, where the authors claim that H3.3 incorporation is dependent on cell cycle state but do not sufficiently test whether this is linked to changes in HIRA levels. Given the importance of HIRA in H3.3 deposition, its levels should be examined in Slbp, Zelda, and Chk1 RNAi embryos to verify whether changes in H3.3 incorporation correlate with HIRA function. Without this, it is difficult to conclude that the observed effects are strictly due to cell cycle regulation rather than histone chaperone dynamics. Since H3.3 incorporation is unaffected in the Slbp and Zelda-RNAi lines there is no reason to suspect a change in HIRA function. There are no available tools (antibodies or fluorescently tagged proteins) to directly measure HIRA protein in Drosophila. To test if changes in HIRA loading might contribute to the decreased H3.3 incorporation in the Chk1 mutant we propose to perform RT-qPCR for HIRA in wildtype and Chk1 embryos. Several figures require additional statistical analyses to support the claims made. In Figure 1B, statistical testing should be included to validate the reported differences. Figure 1C-D states that "H3.3 accumulation reduces more slowly than H3," yet there is no quantitative comparison to substantiate this claim. Similarly, Figure 1E presents the conclusion that "These changes in nuclear import and incorporation result in a less dramatic loss of the free nuclear H3.3 pool than previously seen for H3," despite the fact that H3 data are not included in this figure. The conclusions drawn from these data need to be supported with appropriate statistical comparisons and more precise descriptions of what is being measured. For Figure 1B (now 2B) we do not feel that it is appropriate to directly compare the intensities of the H3-Dendra2 construct expressed from the pseudo-endogenous locus to the H3.3 and chimeric proteins expressed from the H3.3A locus as they were imaged using different settings and therefore we do not feel that direct statistical tests are appropriate. Rather, we plot the two histones on the same graph normalized to their own NC10 values so that the trend in their decrease over time may be compared. The statistical tests for H3.3 compared to the chimeras which were originally in the supplemental table have been added to Figure 3 (formerly figure 2). Revision Plan It is important to note that in this directly comparable situation the ASVM mutant (whose trends closely mirror H3) is highly statistically distinct from H3.3. We have added a note to the legend of the new Figure 1 explaining this which reads: “Note that statistical comparisons between the two Dendra2 constructs have not been done as they were expressed from different loci and imaged under different experimental settings.” For Figure 1C-D (now 2C-D) we have removed this claim from the text. We were referring to the plateau in nuclear import for H3 that is less dramatic in H3.3, but this is more carefully discussed in the next paragraph and its addition at that point generated confusion. The text now reads: “To further assess how nuclear uptake dynamics changed during these cycles, we tracked total nuclear H3 and H3.3 in each cycle (Figure 2C-D). Since nuclear export is effectively zero, we attribute the increase in total H3.3 over time solely to import and therefore the slope of total H3.3 over time corresponds to the import rate. Though the change in initial import rates between NC10 and NC13 are similar between the two histones (Figure S1F), we observed a notable difference in their behavior in NC13. H3 nuclear accumulation plateaus ~5 minutes into NC13, whereas H3.3 nuclear accumulation merely slows (Figure 2C-D).” lines 109-116 For Figure 1E (now 2E), to address the difference between H3 and H3.3 free pools we have added the previously published values to the text and changed the phrasing from “less dramatic” to “less complete”. The sentence now reads: “These changes in nuclear import and incorporation result in a less complete loss of the free nuclear H3.3 pool (~70% free in NC11 to ~30% in NC13) than previously seen for H3 (~55% free in NC11 to ~20% in NC13)” lines 116-119 Figure 2 presents additional concerns regarding data interpretation. The comparisons between H3.3 and H3.3S31A to H3 and H3.3SVM/ASVM lack statistical analysis, making it difficult to determine the significance of the observed differences. As discussed above, it is not appropriate to directly compare H3 to H3.3 and the chimeras at the H3.3A locus since they are expressed from different promoters and imaged with different settings. The ANOVA comparisons between all of the constructs in the H3.3A locus can be found in the supplemental table. We have also added the statistical significance between each chimera and H3.3 within a cell cycle to the figure. Including the full set of comparisons for all genotypes and timepoints makes the figure nearly impossible to interpret, but they remain available in the supplemental table. Revision Plan The disappearance of H3.3 from mitotic chromosomes in Figure 2E is also not explained. If this phenomenon is functionally relevant, the authors should provide a mechanistic interpretation, or at the very least, discuss potential explanations in the text. In Figures 2F-H, the reasoning behind comparing the nuclear intensity of H3.3 to H3 in Hira mutants is unclear. To properly assess the role of HIRA in H3.3 chromatin accumulation, a more appropriate comparison would be between wild-type H3.3 and H3.3 levels in Hira knockdown embryos. As explained in the text and depicted in Figure 3D (formerly 2D), the HIRAssm mutant is a point mutation that prevents observable H3.3 chromatin incorporation, but not nuclear import. This is what is depicted in Figure 3E (formerly 2E). The loss of H3.3 from mitotic chromatin is due to the inability to incorporate H3.3 into chromatin as expected for a HIRA mutant. We have edited the figure 3 legend to make this more clear. It now reads: “Hirassm mutation nearly abolishes the observable H3.3 on mitotic chromatin (E).” In Figure 3F (formerly 2F-H) we ask what happens to H3 chromatin incorporation when there is almost no incorporation of H3.3 due to the HIRA mutation. In this mutant there is so little H3.3 incorporation that we cannot quantify H3.3 levels on mitotic chromatin (see the new Figure 1B for the stage where chromatin levels are quantified). This experiment was done to test if H3.3ASVM (expressed at the H3.3A locus) is incorporated into chromatin in embryos lacking the function of H3.3’s canonical chaperone. We have edited the text to make this more clear: “Since the chromatin incorporation of the H3/H3.3 chimeras appears to depend on their chaperone binding sites, we asked if impairing the canonical H3.3 chaperone, Hira, would affect the incorporation of H3.3ASVMexpressed from the H3.3A locus.”lines 158-160 A broader concern is that the authors only test HIRA as a histone chaperone but do not consider alternative chaperones that could influence H3.3 deposition. Since multiple chaperone systems regulate histone incorporation, it would strengthen the conclusions if additional chaperones were tested. Since HIRAssm reduced H3.3-Dendra2 incorporation to nearly undetectable levels (Figure 3E) we believe that it is the primary H3.3 incorporation pathway during this period of development. Therefore, we believe that removing HIRA function is a sufficient test of the dependance of H3.3ASVM on the major H3.3 chaperone at this time. Although it would be interesting to fully map how all H3 and H3.3 chimera constructs respond to all histone chaperone pathways, we believe that this is beyond the scope of this manuscript. Additionally, the manuscript does not include any validation of the RNAi knockdown efficiencies used throughout the study. This raises concerns about whether the observed phenotypes are truly due to target gene depletion or off-target effects. RT-qPCR or Western blot analyses should be performed to confirm knockdown efficiency. Revision Plan Both the Zelda and slbp-RNAi lines used for knockdowns have been used and validated in the early fly embryo in previously published works ((Yamada et al., 2019), (Duan et al., 2021), (O’Haren et al., 2025), (Chari et al, 2019)) and the phenotypes that we observe in our embryos are consistent with the published data including altered cell cycle durations (Figure S4C) and lack of cellularization/gastrulation. We note that the zelda RNAi phenotypes are also highly consistent with the effects of Zelda germline clones. To validate that slbp-RNAi knocks down histones we included a western blot for Pan-H3 in slbp-RNAi embryos that demonstrates a large effect on total H3 levels (Figure S4A). To further demonstrate the phenotypic effects of the slbp-RNAi we have added supplemental movies (Videos 4 and 5). To fully characterize the RNAi efficiency under our conditions we propose to perform RT-qPCR for slbp in slbp-RNAi and Zelda in Zelda-RNAi compared to control (w) RNAi embryos. Finally, the section discussing "H3.3 incorporation depends on cell cycle state, but not cell cycle duration" is unclear. The term "cell cycle state" is vague and should be explicitly defined. Does this refer to a specific phase of the cell cycle, changes in chromatin accessibility, or another regulatory mechanism? The term cell cycle state is deliberately vague. We know that Chk1 regulates many aspects of cell cycle progression and cannot determine from our data which aspect(s) of cell cycle regulation by Chk1 are important for H3.3 incorporation. Our data indicate that it is not simply interphase duration as we originally hypothesized. We have expanded our discussion section to underscore some aspects of Chk1 regulation that we speculate may be responsible for the change in H3.3 behavior. “Chk1 mutants decrease H3.3 incorporation even before the cell cycle is significantly slowed. Cell cycle slowing has been previously reported to regulate the incorporation of other histone variants in Drosophila15. However, our results indicate that cell cycle state and not duration per se, regulates H3.3 incorporation. In most cell types, the primary role of Chk1 is to stall the cell cycle to protect chromatin in response to DNA damage. Therefore, Chk1 activity directly or indirectly affects the chromatin state in a variety of ways. We speculate that Chk1’s role in regulating origin firing may be particularly important in this context73,74. Late replicating regions and heterochromatin first emerge during ZGA, and Chk1 mutants proceed into mitosis before the chromatin is fully replicated22,23,25,71. Since H3.3 is often associated with heterochromatin, the decreased H3.3 incorporation in Chk1 mutants may be an indirect result of increased origin firing and decreased heterochromatin formation73,74.” lines 287-298 Reviewer #2 (Significance (Required)): This manuscript investigates the regulation of H3.3 incorporation during zygotic genome Revision Plan activation (ZGA) in Drosophila, proposing that the nuclear-to-cytoplasmic (N/C) ratio plays a central role in this process. While the study is conceptually interesting, several concerns arise regarding the lack of proper control experiments and the clarity of the writing. The manuscript is difficult to follow due to vague descriptions, insufficient distinctions between established knowledge and novel findings, and a lack of rigorous statistical analyses. These issues need to be addressed before the study can be considered for publication. Reviewer #3 (Evidence, reproducibility and clarity (Required)): Summary: Based on previous findings of the changing ratios of histone H3 to its variant H3.3, the authors test how H3.3 incorporation into chromatin is regulated for ZGA. They demonstrate here that H3 nuclear availability drops and replacement by H3.3 relies on chaperone binding, though not on its typical chaperone Hira. Furthermore, they show that nuclear-cytoplasmic (N/C) ratios can influence this histone exchange likely by influencing cell cycle state. We thank the reviewer for their thoughtful comments. We note that our data ARE consistent with H3.3 incorporation depending on Hira through its chaperone binding site. Major comments: 1. The claims are largely supported by the data but I think a couple more experiments could help bolster the claims about cell cycle and chk1 regulation. a. Creating a phosphomimetic of the chk1 phosphorylation site on H3.3 to see if it can overcome the defects seen in chk1 mutants b. Assessing heterochromatin of embryos without chk1 (or ASVM mutants) for example, by looking at H3K9me3 levels The first experiments could take several months if the flies haven't already been generated by the authors but the second should be quicker. a. This is an excellent experimental suggestion which is bolstered by the fact that in frogs H3.3 S31A cannot rescue H3.3 morpholino during gastrulation, but H3.3S31D can (Sitbon et al, 2020). However, to correctly conduct this experiment would require generating and validating multiple additional endogenous H3.3 replacement lines, likely without a fluorescent tag as they can interfere with histone rescue constructs in most species. As the reviewer notes, this would take several months of work (we have not generated the critical flies yet) and may not yield a satisfying answer since there are reports that H3.3 may be dispensable in flies aside from as a source of H3-type histone outside of S-phase (Hödl and Bassler, 2012). While we hope to continue experiments along these lines in the future we feel that this is beyond the scope of the current manuscript. Revision Plan b. To address this we propose to stain for H3K9me3 in wildtype and Chk1-/- embryos. Since the ASVM line is not a full replacement of all H3.3 we think that staining for H3K9me3 in this line is unlikely to yield a detectable difference. 2. It would also be interesting to see what the health of the flies with some mutations in this paper are beyond the embryo stage if they are viable (e.g., development to adulthood, fertility etc.) a. the SVM, ASVM mutations b. the hira + ASVM mutations The authors might already have this data but if not they have the flies and it shouldn't take long to get these data. a. To address this concern we propose to conduct hatch rate assays for embryos from the Dendra tagged H3.3, S31A, SVM, ASVM flies. However, we do note that in our experiments only one copy of the H3.3A locus was mutated and tagged with Dendra2 leaving one copy of H3.3A and both copies of H3.3B untouched to ensure normal development as tagging all copies of histone genes can lead to lethality. b. All Hira mutants develop as haploids due to the inability to decondense the sperm chromatin (which is dependent on Hira). This leads to one extra division to restore the N/C ratio prior to cell cycle slowing and ZGA. These embryos go on to gastralate and die late in development after cuticle formation (presumably due to their decreased ploidy) (Loppin et al., 2000). The addition of ASVM into the Hira background does not appear to rescue the ploidy defect as these embryos also undergo the extra division (Figure 3H). We are therefore confident that these embryos will not hatch. We have added the information about the development of Hira mutant to the text as follow: “These embryos develop as haploids and undergo one additional syncytial division before ZGA (NC14). Hirassmembryos develop otherwise phenotypically normally through organogenesis and cuticle formation, but die before hatching57.” lines 164-167 3. In the discussion section, can the authors speculate on how they think H3.3 ASVM is getting incorporated if not through Hira. Are there other known H3 variant chaperones, or can the core histone chaperone substitute? We have expanded our discussion to include the the following: “In the case of the chimeric histone proteins the incorporation behavior was dependent on the chaperone binding site. For example, H3.3ASVM import and incorporation was similar to H3 in control embryos and H3.3ASVM was still incorporated in Hirassm mutants. This is consistent with the chaperone binding site determining the chromatin incorporation pathway and suggests that H3.3ASVM likely interacts with H3 chaperones such as Caf1.” lines 280-285 Revision Plan Minor comments: While the paper is well written, I found the figures very confusing and difficult to interpret. Comments here are meant to make it easier to interpret. 1. Fig 1 and most of the paper would benefit from a schematic of early embryo transitions labelled with time and stages of cell cycle to make interpreting data easier This is an excellent suggestion! We have added a new figure (Figure 1) to explain both the biological system and the way that we measured many properties in this paper. 2. Fig 1- same green color is used for nuclear cycle 12 and for H3.3 making it confusing when reading graphs. Please check other figures where there is a similar use of color for two different things We have changed the colors so that they are more distinct. 3. Fig 1C,D might benefit more from being split up into 3 graphs by cell cycle with H3 and H3.3 plotted on the same graphs rather than the way it is now We do not feel that it is appropriate to directly compare the intensities of the H3-Dendra2 construct expressed from the pseudo-endogenous locus to the H3.3 and chimeric proteins expressed from the H3.3A locus as they were imaged using different settings. These curves can be directly compared within a construct and we can evaluate their trends over time, but the normalized values should not be directly compared in the way that would be encouraged by plotting the data as suggested. 4. Line 130-133: can they also comment on the different between SVM and ASVM. It seems like SVM might be even worse than ASVM (Fig 2C). Is this related to chk1 phosphorylation? We think that this is a property of the mixed chimeras since S31A is also imported less efficiently than H3.3 (though we cannot be sure without further experiments). We have added this explanation to the text: “We speculate that chimeric histone proteins (H3.3S31A and H3.3SVM) are not as efficiently handled by the chaperone machinery as species that are normally found in the organism including H3.3ASVM which is protein-identical to H3.” lines 150-152 5. Fig 2F-G: It is very difficult to compare between histones when they are on different graphs, please consider putting H3, H3.3 and H3.3ASVM in a hirassm background on the same graph. We have done this in the new Figure 3F. Revision Plan 6. Fig 3- move G to become A and then have A and B. We have restructured this figure to include the nuclear density map of control in response to a comment from Reviewer 1. Although not exactly what the reviewer has envisioned, we hope that this adds clarity to the figure. 7. The initial slope graphs in 4D, E, H and I are not easy to understand and would benefit from an explanation in the legend. We have edited the legend of Figure 5D (formerly 4D) and S1F which now read: “Initial slopes of nuclear import curves (change in total nuclear intensity over time for the first 5 timepoints) …” In addition we have updated the methods to include: “Import rates were calculated by using a linear regression for the total nuclear intensity over time for the first 5 timepoints in the nuclear import curves.” lines 471-473, methods Reviewer #3 (Significance (Required)): This paper addresses an important and understudied question- how do histones and their variants mediate chromatin regulation in the early embryo before zygotic genome activation? The authors follow up on some previous findings and provide new insights using clever genetics and cell biology in Drosophila melanogaster. However, the authors do not directly look at chromatin structural changes using existing genomic tools. This may be beyond the scope of this work but would make for a nice addition to strengthen their claims if they can implement these chromatin accessibility techniques in the early embryo. Histones affect a majority of biological processes and understanding their role in the early embryo is key to understanding development. I believe this study applies to a broad audience interested in basic science. However, I do think the authors might benefit from a more broad discussion of their results to attract a broad readership.
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Nevertheless, migrating from JUnit 4 to 5 requires effort. All annotations, like @Test, now reside in the package org.junit.jupiter.api , and some annotations were renamed or dropped and have to be replaced. A short overview of the differences between both framework versions is the following: Assertions reside in org.junit.jupiter.api.Assertions Assumptions reside in org.junit.jupiter.api.Assumptions @Before and @After no longer exist; use @BeforeEach and @AfterEach instead. @BeforeClass and @AfterClass no longer exist; use @BeforeAll and @AfterAll instead. @Ignore no longer exists, use @Disabled or one of the other built-in execution conditions instead @Category no longer exists, use @Tag instead @Rule and @ClassRule no longer exist; superseded by @ExtendWith and @RegisterExtension @RunWith no longer exists, superseded by the extension model using @ExtendWith
JUnit 4 到 5 的主要变化
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bookshelf.vitalsource.com bookshelf.vitalsource.com
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file is named, for the convenience of its human users, and is referred to by its name. A name is usually a string of characters, such as example.c. Some systems differentiate between uppercase and lowercase characters in names, whereas other systems do not. When a file is named, it becomes independent of the process, the user, and even the system that created it. For instance, one user might create the file example.c, and another user might edit that file by specifying its name. The file's owner might write the file to a USB drive, send it as an e-mail attachment, or copy it across a network, and it could still be called example.c on the destination system. Unless there is a sharing and synchonization method, that second copy is now independent of the first and can be changed separately. A file's attributes vary from one operating system to another but typically consist of these: Name. The symbolic file name is the only information kept in human-readable form. Identifier. This unique tag, usually a number, identifies the file within the file system; it is the non-human-readable name for the file. Type. This information is needed for systems that support different types of files. Location. This information is a pointer to a device and to the location of the file on that device. Size. The current size of the file (in bytes, words, or blocks) and possibly the maximum allowed size are included in this attribute. Protection. Access-control information determines who can do reading, writing, executing, and so on. Timestamps and user identification. This information may be kept for creation, last modification, and last use. These data can be useful for protection, security, and usage monitoring.
A file has a name for easy identification and can be accessed or moved while keeping the same name. Copies of a file are separate unless they are synchronized. File attributes include its name, a unique system identifier, its type, size, and access permissions. It also has timestamps that record when it was created, modified, or used.
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A file is named, for the convenience of its human users, and is referred to by its name. A name is usually a string of characters, such as example.c. Some systems differentiate between uppercase and lowercase characters in names, whereas other systems do not. When a file is named, it becomes independent of the process, the user, and even the system that created it. For instance, one user might create the file example.c, and another user might edit that file by specifying its name. The file's owner might write the file to a USB drive, send it as an e-mail attachment, or copy it across a network, and it could still be called example.c on the destination system. Unless there is a sharing and synchonization method, that second copy is now independent of the first and can be changed separately. A file's attributes vary from one operating system to another but typically consist of these: Name. The symbolic file name is the only information kept in human-readable form. Identifier. This unique tag, usually a number, identifies the file within the file system; it is the non-human-readable name for the file. Type. This information is needed for systems that support different types of files. Location. This information is a pointer to a device and to the location of the file on that device. Size. The current size of the file (in bytes, words, or blocks) and possibly the maximum allowed size are included in this attribute. Protection. Access-control information determines who can do reading, writing, executing, and so on. Timestamps and user identification. This information may be kept for creation, last modification, and last use. These data can be useful for protection, security, and usage monitoring. Some newer file systems also support extended file attributes, including character encoding of the file and security features such as a file checksum. Figure 13.1 illustrates a file info window on macOS that displays a file's attributes.
File attributes vary across operating systems, but they generally include name, identifier, type, location, size, protection, timestamps, and access permissions. These attributes help manage and secure files effectively. However, the concept of extended attributes, such as file checksums and character encoding, raises questions. How do extended attributes improve security, and how are they implemented differently across file systems? Understanding these attributes is crucial for file management, particularly in environments that require strict access control and data integrity measures. I would like to explore how modern file systems, such as NTFS and ext4, utilize extended attributes to enhance security and organization.
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AI-powered suggestions
Imagine 3d Reading.... something well beyond writing suggestions.
1.) Source material. eg. NY Times. 2.) Social layer e.g. I tag you on a sentence talking about their Grammarly/Coda article and rumors about Notion 3.) Engaging AI to test facts, offer alternative povs, summaries, etc.
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openai.com openai.com
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advanced AI mode
Users can also tag topics and soon @mention their peers as read.
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- Feb 2025
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www.biorxiv.org www.biorxiv.org
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Author response:
The following is the authors’ response to the original reviews.
Reviewer #1 (Public review):
(1) The mechanism by which STAMBPL1 mediates GRHL3 transcription through its interaction with FOXO1 is not sufficiently discussed, especially in relation to how STAMBPL1 regulates FOXO1. Some reported effects are modest.
We appreciate the reviewer’s comments. In response, we have added a discussion on the potential mechanisms by which STAMPBL1 regulates FOXO1 transcriptional activity in Discussion, highlighted in red on page 18, lines 342 to 352. The specific reply content is as follows: “The transcriptional activity of FOXO1 is primarily regulated by its nucleocytoplasmic shuttling process (Van Der Heide, Hoekman et al. 2004). The PI3K/AKT pathway promotes the phosphorylation of FOXO1, resulting in the formation of a complex with members of the 14-3-3 family (including 14-3-3σ, 14-3-3ε, and 14-3-3ζ), which facilitates its export from the nucleus and inhibits its transcriptional activity (Huang and Tindall 2007, Tzivion, Dobson et al. 2011). It’s reported that TDAG51 prevents the binding of 14-3-3ζ to FOXO1 in the nucleus by interacting with FOXO1, thereby enhancing its transcriptional activity through increased accumulation within the nucleus (Park, Jeon et al. 2023). Our results indicate that the overexpression of STAMBPL1 and STAMBPL1-E292A did not affect the protein levels of FOXO1 (Fig.7E and Fig.S5E), but STAMBPL1 co-localizes with FOXO1 in the nucleus (Fig.7M) and interacts with it (Fig.7N and Fig.S5I-J). This suggests that STAMBPL1 enhances the transcriptional activity of FOXO1 on GRHL3 by interacting with nuclear FOXO1.” The result was added to Supplementary Figure 5 as Fig.S5E.
Reviewer #2 (Public review):
(1) A potential limitation of the study is the reliance on specific cellular and animal models, which may constrain the extrapolation of these findings to the broader spectrum of human TNBC biology. Furthermore, while the study provides evidence for a novel regulatory axis involving STAMBPL1, FOXO1, and GRHL3, the multifaceted nature of angiogenesis may implicate additional regulatory factors not exhaustively addressed in this research.
We appreciate the valuable suggestions provided by the reviewer. In Discussion, we have added an in-depth discussion of the limitations of the study, as well as an analysis of the regulatory factors related to tumor angiogenesis, which highlighted in red on pages 20 to 21, lines 396 to 412. The relevant content added is as follows: “In this study, we utilized two triple-negative breast cancer cell lines, HCC1806 and HCC1937, along with human primary umbilical vein endothelial cells (HUVECs) and a nude mouse breast orthotopic transplantation tumor model to investigate the regulatory mechanism by which STAMBPL1 activates the GRHL3/HIF1α/VEGFA signaling pathway through its interaction with FOXO1, thereby promoting angiogenesis in TNBC. The results of this study have certain limitations regarding their applicability to human TNBC biology. Furthermore, in addition to the HIF1α/VEGFA signaling pathway emphasized in this study, tumor cells can continuously release or upregulate various pro-angiogenic factors, such as Angiopoietin and FGF, which activate endothelial cells, pericytes (PCs), cancer-associated fibroblasts (CAFs), endothelial progenitor cells (EPCs), and immune cells (ICs). This leads to capillary dilation, basement membrane disruption, extracellular matrix remodeling, pericyte detachment, and endothelial cell differentiation, thereby sustaining a highly active state of angiogenesis (Liu, Chen et al. 2023). It is important to collect clinical TNBC tissue samples in the future to analyze the expression of the STAMBPL1/FOXO1/GRHL3/HIF1α/VEGFA signaling axis. Furthermore, patient-derived organoid and xenograft models are useful to elucidate the regulatory relationship of this axis in TNBC angiogenesis”
Reviewer #3 (Public review):
The main weaknesses of this work are that the relevance of this molecular axis to the pathogenesis of TNBC is not clear, and it is not clearly established whether this is a regulatory pathway that occurs in hypoxic conditions or independently of oxygen levels.
(1) With respect to the first point, both FOXO1 and GRHL3 have been previously described as tumor suppressors, with reports of FOXO1 inhibiting tumor angiogenesis. Therefore, this works describes an apparently contradictory function of these proteins in TNBC. While it is not surprising that the same genes perform divergent functions in different tumor contexts, a stronger evidence in support of the oncogenic function of these two genes should be provided to make the data more convincing. As an example, the data in support of high STAMBPL1, FOXO and GRHL3 gene expression in TNBC TCGA specimens provided in Figure 8 is not very strong and it is not clear what the non-TNBC specimens are (whether other breast cancers or other tumors, perhaps those tumors whether these genes perform tumor suppressive functions). To strengthen the notion that STAMBPL1, FOXO and GRHL3 are overexpressed in TNCB, the authors could provide a comparison with normal tissue, as well as the analysis of other publicly available datasets (like the NCI Clinical Proteomic Tumor Analysis Consortium as an example). Finally, is it not clear what are the basal protein expression levels of STAMBPL1 in the cell lines used in this study, as based on the data presented in Figures 2D and F it appears that the protein is not expressed if not exogenously overexpressed. It would be helpful if the authors addressed this issue and provided further evidence of STAMBPL1 expression in TNBC cell lines.
We appreciate the suggestions. In this study, we utilized the BCIP online tool to analyze the Metabric database, incorporating adjacent normal tissues as controls. Although the expression levels of STAMBPL1, FOXO1, and GRHL3 in breast cancer tissues are not uniformly higher than those in adjacent tissues, their expression levels in triple-negative breast cancer (TNBC) are significantly elevated compared to non-TNBC. The results of this re-analysis have been added in Supplementary Figure 6 as Fig.S6A-C.
About the question of the basal protein expression levels of STAMBPL1 in the cell lines used in this study, our response is that Fig. 2A showed the endogenous level of STAMBPL1 in HCC1806 and HCC1937. For Fig. 2D and 2F, the overexpressed STAMBPL1 was fused with a 3xFlag tag, resulting in a higher molecular weight compared to the endogenous STAMBPL1. In the revised Figure 2, we have indicated the positions of the endogenous (Endo.) and exogenous (OE.) STAMBPL1 bands with arrows.
(2) Linked to these considerations is the second major criticism, namely that it is not made clear if this new regulatory axis is proposed to act in normoxic or hypoxic conditions. The experiments presented in this paper are performed in both conditions but a clear explanation as to why cells are exposed to hypoxia is not given and would be necessary being that HIF-1a transcription and not protein stability is being analyzed. Also, different hypoxic conditions are sometimes used, resulting in different mRNA levels of HIF-1a and its downstream targets and quite significant fluctuations within the same cell line from one experimental setting to the next. The authors should provide an explanation as to why experimental conditions are changed and, more importantly, the experiments presented in Figure 2 should be performed also in normoxia.
Thanks for the comments. Under normoxic conditions, HIF1α is recognized by pVHL due to hydroxylation and is rapidly degraded via the proteasomal pathway. In contrast, under hypoxic conditions, HIF1α protein is accumulated. To investigate the effect of STAMBPL1 knockdown on HIF1A gene transcription levels, we conducted experiments under hypoxic conditions to avoid interference from the rapid degradation of HIF1α at the protein level, as shown in Figures 2B-C. Furthermore, under normoxic conditions, the overexpression of STAMBPL1 had been demonstrated to significantly enhance the protein levels of HIF1α and upregulate the transcription of VEGFA through HIF1α. To avoid the potential impact of excessive accumulation of HIF1α protein under hypoxic conditions on its protein level detection and the transcription of downstream VEGFA, the related experiments shown in Figure 2D-G were performed under normoxic conditions. We have explained the corresponding experimental conditions in the “Result” and “Figure legends” according to the reviewer's comments, highlighted in red.
(3) Another critical point is that necessary experimental controls are sometimes missing, and this is reducing the strength of some of the conclusions enunciated by the authors. As examples, experiments where overexpression of STAMBPL1 is coupled to silencing of FOXO1 to demonstrate dependency lack FOXO1 silencing the absence of STAMBPL1 overexpression. Because diminishing FOXO1 expression affects HIF-1a/VEGF transcription even in the absence of STAMBPL1 (shown in Figure 7C, D), it is not clear if the data presented in Figure 7G are significant. The difference between HIF-1a expression upon FOXO1 silencing should be compared in the presence or absence of STAMBPL1 overexpression to understand if FOXO1 impacts HIF-1a transcription dependently or independently of STAMBPL1.
Thank you for this comment. For Fig.7G-H, our experimental objective was to determine whether the activation of HIF1A/VEGFA transcription by STAMBPL1 via FOXO1. Therefore, under STAMBPL1 overexpression, we knocked down FOXO1 to investigate whether FOXO1 silencing could reverse the upregulation of HIF1A/VEGFA transcription induced by STAMBPL1 overexpression.
(4) In addition, some minor comments to improve the quality of this manuscript are provided.
(4.1) As a general statement, the manuscript is extremely synthetic. While this is not necessarily a negative feature, sometimes results are discussed in the figure legends and not in the main text (as an example, western blots showing HIF-1a expression) and this makes it hard to read thought the data in an easy and enjoyable manner.
Thank you for this suggestion. We have revised the figure legends to make them clearer and more concise, highlighted in red.
(4.2) The effect of STAMBPL1 overexpression on HIF-1a transcription is minor (Figure 2) The authors should explain why they think this is the case and whether hypoxia may provide a molecular environment that is more permissive to this type of regulation.
Thank you for the comment. Under normoxic conditions, we conducted WB to examine the protein expression of HIF1α after the overexpression of STAMBPL1 and the knockdown of HIF1α. To visually illustrate the impact of STAMBPL1 overexpression on HIF1A protein levels, as well as the effectiveness of HIF1α knockdown, we annotated the grayscale analysis results of the bands in Figures 2D and 2F. As the reviewer pointed out, under normoxic conditions, HIF1α is rapidly degraded, which may explain why the upregulation of HIF1α protein levels by STAMBPL1 overexpression is not very pronounced.
(4.3) HIF-1a does not appear upregulated at the protein level protein by STAMBPL1 or GRLH3 overexpression, even though this is stated in the legends of Figures 2 and 6. The authors should show unsaturated western blots images and provide quantitative data of independent experiments to make this point.
Thank you for this comment. We have added the unsaturated image of HIF1α into Fig.2D, and performed a grayscale analysis of the HIF1α bands in Fig.2D and Fig.6A to indicate the relative protein level of HIF1α.
Reviewer #1 (Recommendations for the authors):
(1) The authors previously reported that STAMBPL1 stabilizes MKP1 in TNBC. However, in this study, they focus on HIF1a. Given that STAMBPL1 affects HIF1a expression, it would be valuable to examine the levels of ROS in TNBC cells with or without STAMBPL1, as ROS is known to influence HIF1a stability.
Thank you for your comments. It’s known that STAMBPL1 functions as a deubiquitinating enzyme. However, our study reveals that the upregulation of HIF1α by STAMBPL1 is independent of its deubiquitinating activity. This conclusion is supported by the observation that overexpression of the deubiquitinase active site mutant, STAMBPL1-E292A, also upregulated HIF1α expression (Figure 1F). Moreover, STAMBPL1 overexpression enhanced HIF1α transcription (Figures 4E and S3E), while STAMBPL1 knockdown was able to inhibit the transcription of HIF1α (Figures 2B-C). These results indicate that STAMBPL1 mediates the transcription of HIF1α but does not affect the stability of HIF1α. For these reasons, we think that it is unnecessary to examine the ROS levels.
(2) Figure 1A: The regulation of HIF1a mRNA by STAMBPL1, but not its protein levels, could be better addressed by using MG132 to rule out the impact of protein degradation.
Thanks for this comment. Under normoxic conditions, the oxygen-sensitive prolyl hydroxylases PHD1-3 act on HIF1α, specifically inducing hydroxylation at the proline 402 and 564 residues. These hydroxylated residues are recognized by the pVHL/E3 ubiquitin ligase complex, leading to ubiquitination and subsequent degradation via the proteasome pathway. Conversely, under hypoxic conditions, PHD1-3 are inactivated, and non-hydroxylated HIF1α is not recognized by the pVHL/E3 ubiquitin ligase complex, thereby avoiding ubiquitination and proteasomal degradation (DOI: 10.1073/pnas.95.14.7987, DOI: 10.1515/BC.2004.016, and DOI: 10.1042/BJ20040620). The mechanism of HIF1α accumulation under hypoxia is analogous to the action of the proteasome inhibitor MG132. When we treated cells with hypoxia, the ubiquitination and proteasomal degradation pathway of HIF1α was blocked. At this time, STAMBPL1 knockdown could downregulate the expression of HIF1α (Fig.1A). Meanwhile, since the knockdown of STAMBPL1 significantly downregulated the mRNA level of HIF1α under hypoxia (Fig.2B-C), we concluded that STAMBPL1 affects the expression of HIF1α by mediating its transcription. In addition, MG132 will block all proteasomal substrate degradation and may affect HIF1α mRNA levels indirectly.
(3) Figure 2D and 2F: The effect of STAMBPL1 in promoting HIF1a expression is quite mild, and the effect of HIF1a knockdown is also modest. Given the high levels of STAMBPL1 in TNBC cell lines (Figure 2A), it would be better to repeat these experiments in a STAMBPL1-knockdown setting for clearer insights.
We appreciate this insightful suggestion. Considering that the regulation of HIF1α expression by STAMBPL1 occurs at the transcriptional level, and to prevent excessive accumulation of HIF1a during hypoxia that could confound the effect of STAMBPL1 overexpression on HIF1α regulation, we opted to overexpress STAMBPL1 under normoxic conditions and subsequently knock down HIF1α, as shown in Fig.2D and Fig.2F. This approach allowed us to observe that STAMBPL1 overexpression can upregulate HIF1a expression to some extent. Additionally, in response to the reviewer's suggestion to knock down STAMBPL1, we have conducted the corresponding experiments, with results presented in Fig.1A-E and Fig.2B-C.
(4) Figure 4A: Why does the RNA-seq pattern differ significantly between the two siRNAs? Additionally, the authors should clarify why they focus primarily on transcription factors, as other mechanisms, such as mRNA stability and RNA modification, could also influence gene transcription.
Thank you for this comment. Two siRNAs for STAMBPL1 were designed and synthesized by a biotechnology company. Although both siRNAs target STAMBPL1, they target different sequences. While both siRNAs effectively knocked down STAMBPL1 (Fig. 1A and Fig. 2A), the possibility of off-target effects cannot be completely ruled out. Therefore, we needed to use two siRNAs simultaneously for RNA-seq, ensuring that the gene expression changes observed are due to the knockdown of STAMBPL1 by focusing on genes downregulated by both two siRNAs. Additionally, among the 27 genes downregulated by both two siRNAs, only 18 genes were annotated. Of these 18 genes, except for GRHL3, which is a transcription factor reported to be involved in gene transcription regulation, the remaining 17 genes have no documented association with RNA transcription, stability, or modification. Therefore, we focused on the GRHL3 gene.
(5) Figure 5G: To investigate whether STAMBPL1 and GRHL3 function epistatically in the pathway, a double knockdown of STAMBPL1 and GRHL3 should be examined. Additionally, a double knockdown of STAMBPL1 and FOXO1 should be assessed.
Thank you for your comment. In Figure 5G, we aimed to assess the knockdown efficiency of GRHL3 using siRNAs. To determine whether STAMBPL1 upregulates the HIF1a/VEGFA axis via GRHL3, we overexpressed STAMBPL1 and subsequently knocked down GRHL3. Our findings indicated that STAMBPL1 overexpression indeed enhanced the HIF1a/VEGFA axis, which was rescued by the knockdown of GRHL3, as shown in Figures 4E-F and S3E-F. Similarly, upon overexpressing STAMBPL1 and knocking down FOXO1, we observed that STAMBPL1 overexpression increased the GRHL3/HIF1a/VEGFA axis, which could also be rescued by knocking down FOXO1, as shown in Figures 7F-H. These results suggest that STAMBPL1 upregulates the GRHL3/HIF1a/VEGFA axis through FOXO1. We do not think it is a right way to double knock down STAMBPL1 and FOXO1 or GRHL3.
(6) Figure 7: It remains unclear how STAMBPL1 regulates FOXO1. The authors show that STAMBPL1 increases the transcriptional activation of FOXO1 at the GRHL3 promoter, but it is not clear if STAMBPL1 is required for FOXO1 binding to the GRHL3 promoter. To address this, STAMBPL1-knockdown should be included to examine its effect on FOXO1 binding to the GRHL3 promoter. Furthermore, it would be important to determine whether the STAMBPL1-FOXO1 interaction is essential for GRHL3 transcription. Since the interaction sites of STAMBPL1-FOXO1 have been mapped, a mutant disrupting the interaction would provide better insight into how STAMBPL1 promotes GRHL3 transcription by interacting with FOXO1.
Thank you for this comment. It has been reported that FOXO1 promotes the transcription of the GRHL3 gene by interacting with its promoter (DOI: 10.1093/nar/gkw1276). We also verified through ChIP assay that FOXO1 can bind to the promoter of GRHL3 gene (Fig.7I) and mediate its transcription. Specifically, knocking down FOXO1 significantly down-regulated the mRNA level of GRHL3 (Fig.7B), and the GRHL3 promoter lacking FOXO1 binding site almost completely lost transcriptional activity (Fig.7J), indicating that FOXO1 is crucial for the transcriptional activity of the GRHL3 promoter. Overexpression of STAMBPL1 enhances the activating effect of FOXO1 on the transcriptional activity of the GRHL3 promoter (Fig.7K). However, the up-regulation of GRHL3 transcription by overexpression of STAMBPL1 is completely blocked by FOXO1 knockdown (Fig.7F), and the knockdown of FOXO1 essentially blocks the binding of STAMBPL1 to the GRHL3 promoter (Fig.7L), suggesting that STAMBPL1 affects the transcriptional expression of GRHL3 based on FOXO1. As we added in Discussion, the transcription factor activity of FOXO1 is mainly regulated by its nucleoplasm shuttling process, and the accumulation of FOXO1 in nucleus can enhance its transcription factor activity (DOI: 10.1042/BJ20040167; DOI: 10.15252/embj.2022111867). In our research, neither STAMBPL1 nor its mutant of deubiquitinating enzyme site affected the expression of FOXO1 (Fig.S5E), but STAMBPL1 and FOXO1 co-located in the nucleus (Fig.7M), and they interacted with each other (Fig.7N, Fig.S5I-J). Therefore, we speculate that STAMBPL1 interacts with FOXO1 in the nucleus, obstructs the binding of FOXO1 with the members of 14-3-3 family, inhibits the export of FOXO1, thereby enhancing its transcriptional activity. This interaction between STAMBPL1 and FOXO1 does not necessarily affect the binding of FOXO1 with DNA, including the GRHL3 promoter.
(7) Figure 8 A-C: What is the correlation among the expressions of STAMBPL1, FOXO1, and GRHL3 in TNBC tumors compared to non-TNBC tumors?
Thank you for your comment. In Figure 8A-C, we analyzed the expression levels of STAMBPL1, FOXO1, and GRHL3 in both TNBC and non-TNBC samples using the BCIP. The results indicate that the expression levels of these three genes are significantly higher in TNBC compared to non-TNBC samples. To investigate the correlation among the expressions of STAMBPL1, FOXO1, and GRHL3 in TNBC versus non-TNBC, we further utilized the Metabric data. Besides the positive correlation trend between STAMBPL1 and GRHL3 expression in TNBC clinical samples (Pearson R = 0.27), no significant correlation was observed in the expression levels of STAMBPL1, FOXO1, and GRHL3 in TNBC and non-TNBC clinical samples (as shown in Author response image 1 below). Since STAMBPL1 and FOXO1 are involved as protein molecules in the transcriptional regulation of GRHL3 gene, and the data obtained from the Metabric database are the transcriptional levels of these three genes, this might be the reason why the correlation between their expressions was not observed.
Author response image 1.
Reviewer #2 (Recommendations for the authors):
The authors have thoroughly elucidated the role of STAMBPL1 in TNBC. However, it would be beneficial to discuss the potential clinical implications of these findings, such as how targeting STAMBPL1 or FOXO1 might impact current treatment strategies for TNBC. However, several issues need to be addressed.
Major:
(1) While the study provides an exhaustive analysis of the molecular mechanisms, a comparison with other subtypes of breast cancer could enhance our understanding of the specificity of the STAMBPL1/FOXO1/GRHL3/HIF1α/VEGFA axis in TNBC.
Thank you for your comment. According to report, STAMBPL1 is significantly associated with the mesenchymal characteristics of breast cancer (DOI: 10.1038/s41416-020-0972-x). We utilized cBioPortal (http://www.cbioportal.org/) to analyze the expression of STAMBPL1 across various clinical subtypes of breast cancer. The results indicated that STAMBPL1 is highly expressed in invasive breast cancer, which has been added to Supplementary Figure 6 as Fig.S6D. Given that TNBC is an aggressive type of invasive breast cancer, we further examined the expression of STAMBPL1 in TNBC compared to non-TNBC using BCIP (http://omicsnet.org/bcancer/database). Our findings revealed that the expression level of STAMBPL1 in TNBC was elevated relative to its levels in non-TNBC (Fig.8A). Additionally, since tumor angiogenesis is a critical factor influencing the metastasis of cancer cells, our study focused specifically on the pro-angiogenic effects of STAMBPL1 in TNBC.
(2) The authors might consider discussing any potential off-target effects of the siRNA and shRNA used in the study to bolster the conclusions drawn from the knockdown experiments.
We appreciate the reviewer's suggestion. It is well-known that siRNA or shRNA have off-target effects. To address this concern, we employed two siRNAs for each gene knockdown in our study. Specifically, we knocked down genes such as STAMBPL1, FOXO1, GRHL3, and HIF1A in two TNBC cell lines, HCC1806 and HCC1937, using two siRNAs. Except for siRNA#1 targeting HIF1A, which did not show a significant knockdown effect in HCC1806 cells (Fig.2D and Fig.6A), the knockdown effects of other siRNAs on their respective genes were effective, and the resulting phenotypes were consistent. As shown in Fig.2F and Fig.S4H, siRNA#1 targeting HIF1A had a significant knockdown effect in HCC1937 cells. The lower knockdown efficiency of this siRNA in HCC1806 cell line might be attributed to cell-specific factors.
(3) It would be advantageous if the authors could provide further details on the patient demographics and tumor characteristics in the TCGA database analysis to better comprehend the clinical relevance of their findings.
Thanks for the reviewer's suggestions. We have now indicated the number of clinical samples in each group in the legend of Fig.8A-C. Since we utilized the BCIP online database to analyze and compare the expression levels of the three genes STAMBPL1, FOXO1, and GRHL3 in TNBC and non-TNBC, we are unable to obtain more specific information regarding the tumor characteristics of each sample. However, our analysis clearly shows that the expression levels of these three genes are significantly higher in TNBC compared to non-TNBC.
(4) The authors should consider discussing any limitations regarding the generalizability of their findings, such as potential variations among different TNBC subtypes or the specificity of their observations to certain stages of the disease.
We appreciate the reviewer's comment. Accordingly, we have added a discussion on the limitation of this study in Discussion, highlighted in red font on pages 20 to 21, lines 396 to 412. In addition, we utilized the bc-GenExMiner online database to conduct a comparative analysis of STAMBPL1 expression in different subtypes of non-TNBC and TNBC. The result indicates that STAMBPL1 is highly expressed in mesenchymal-like and basal-like TNBC, which has been added into Supplementary Figure 6 as Fig.S6E. Since these two subtypes of TNBC are highly invasive and metastatic, it suggests that targeting the signaling pathway of STAMBPL1/FOXO1/GRHL3/HIF1α/VEGFA may offer clinical benefits for patients with invasive TNBC.
Minor:
The paper is generally well-written, but it's crucial to maintain vigilance for subject-verb agreement, proper use of tense, and consistent terminology.
Thank you for this suggestion. We have thoroughly revised the article for issues such as grammar, including tense, subject-verb agreement, and terminology.
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hancockcollege.instructure.com hancockcollege.instructure.com
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Now a major bank has put a price tag on how much the economy has lost as a result of discrimination against African Americans: $16 trillion.
Thesis the united states has lost a lot of money due to racism and discrimination.
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cautious-robot-m6r6m2e.pages.github.io cautious-robot-m6r6m2e.pages.github.io
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Tag the other devs to be Reviewers (at least 1 reviewer is required for approval, for larger Issues request that multiple reviewers need to approve it)
What is the process for determining who will review (if only 1 reviewer is needed)?
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www.biorxiv.org www.biorxiv.org
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Author response:
The following is the authors’ response to the original reviews.
Reviewer #1 (Public review):
Fuchs describes a novel method of enzymatic protein-protein conjugation using the enzyme Connectase. The author is able to make this process irreversible by screening different Connectase recognition sites to find an alternative sequence that is also accepted by the enzyme. They are then able to selectively render the byproduct of the reaction inactive, preventing the reverse reaction, and add the desired conjugate with the alternative recognition sequence to achieve near-complete conversion. I agree with the authors that this novel enzymatic protein fusion method has several applications in the field of bioconjugation, ranging from biophysical assay conduction to therapeutic development. Previously the author has published on the discovery of the Connectase enzymes and has shown its utility in tagging proteins and detecting them by in-gel fluorescence. They now extend their work to include the application of Connectase in creating protein-protein fusions, antibody-protein conjugates, and cyclic/polymerized proteins. As mentioned by the author, enzymatic protein conjugation methods can provide several benefits over other non-specific and click chemistry labeling methods. Connectase specifically can provide some benefits over the more widely used Sortase, depending on the nature of the species that is desired to be conjugated. However, due to a similar lengthy sequence between conjugation partners, the method described in this paper does not provide clear benefits over the existing SpyTag-SpyCatcher conjugation system. Additionally, specific disadvantages of the method described are not thoroughly investigated, such as difficulty in purifying and separating the desired product from the multiple proteins used. Overall, this method provides a novel, reproducible way to enzymatically create protein-protein conjugates.
The manuscript is well-written and will be of interest to those who are specifically working on chemical protein modifications and bioconjugation.
I'd like to comment on two points.
(1) The benefits over the SpyTag-SpyCatcher system. Here, the conjugation partners are fused via the 12.3 kDa SpyCatcher protein, which is considerably larger than the Connectase fusion sequence (19 aa). This is mentioned in the introduction (p. 1 ln 24-26). Furthermore, SpyTag-SpyCatcher fusions are truly irreversible, while Connectase/BcPAP fusions may be reversed (p. 8, ln 265-273). For example, target proteins (e.g., AGAFDADPLVVEI-Protein) may be covalently fused to functionalized magnetic beads (e.g., Bead-ELASKDPGAFDADPLVVEI) in order to perform a pulldown assay. After the assay, the target protein and any bound interactors could be released from the beads by the addition of a Connectase / peptide (AGAFDAPLVVEI) mixture.
In a related technology, the SpyTag-SpyCatcher system was split into three components, SpyLigase, SpyTag and KTag (Fierer et al., PNAS 2014). The resulting method introduces a sequence between the fusion partners (SpyTag (13aa) + KTag (10aa)), which is similar in length to the Connectase fusion sequence (p. 8, ln 297 - 298). Compared to the original method, however, this approach seems to require longer incubation times, while yielding less fusion product (Fierer et al., Figure 2).
(2) Purification of the fusion product. The method is actually advantageous in this respect, as described in the discussion (p. 8, ln 258-264). Examples are now provided in Figure 6.
Reviewer #2 (Public review):
Summary:
Unlike previous traditional protein fusion protocols, the author claims their proposed new method is fast, simple, specific, reversible, and results in a complete 1:1 fusion. A multi-disciplinary approach from cloning and purification, biochemical analyses, and proteomic mass spec confirmation revealed fusion products were achieved.
Strengths:
The author provides convincing evidence that an alternative to traditional protein fusion synthesis is more efficient with 100% yields using connectase. The author optimized the protocol's efficiency with assays replacing a single amino acid and identification of a proline aminopeptidase, Bacilius coagulans (BcPAP), as a usable enzyme to use in the fusion reaction. Multiple examples including Ubiquitin, GST, and antibody fusion/conjugations reveal how this method can be applied to a diverse range of biological processes.
Weaknesses:
Though the ~100% ligation efficiency is an advancement, the long recognition linker may be the biggest drawback. For large native proteins that are challenging/cannot be synthesized and require multiple connectase ligation reactions to yield a complete continuous product, the multiple interruptions with long linkers will likely interfere with protein folding, resulting in non-native protein structures. This method will be a good alternative to traditional approaches as the author mentioned but limited to generating epitope/peptide/protein tagged proteins, and not for synthetic protein biology aimed at examining native/endogenous protein function in vitro.
The assessment is fair, and I have no further comments to add.
Reviewer #1 (Recommendations for the authors):
Major/Experimental Suggestions:
(1) Throughout the paper only one reaction shown via gels had 100% conversion to desired product (Figure 3C). It is misleading to title a paper with absolutes such as "100% product yield", when the majority of reactions show >95% product yield, without any purification. Please change the title of the manuscript to something along the lines of "Novel Irreversible Enzymatic Protein Fusions with Near-Complete Product Yield".
The conjugation reaction is thermodynamically favored. It is driven by the hydrolysis of a peptide bond (P|GADFDADPLVVEI), which typically releases 8 - 16 kJ/mol energy. This should result in a >99.99% complete reaction (DG° = -RT ln (Product/Educt)). In line with this, 99% - 100% of the less abundant educts (LysS, Figure 3A; MBP, Figure 3B; Ub-Strep, Figure 3C) are converted in the time courses (Figure 3D-F show different reaction conditions, which slow down conjugate formation). 100% conversion are also shown in Figure 5, Figure 6, and Figure S4. Likewise, 99.6% relative fusion product signal intensity in an LCMS analysis (Figure S2) after 4h reaction time (0.13% and 0.25% educts). In this experiment, the proline had been removed from 99.8% of the peptide byproducts (P|GADFDADPLVVEI). It is clear that this reaction is still ongoing and that >99.99% of the prolines will be removed from the peptides in time. These findings suggest that the conjugation reaction gradually slows down the less educt is available, but eventually reaches completion.
For some experiments, lower product yields (e.g. 97% in Figure 3B) are reported in the paper. These were calculated with Yield = 100% x Product / (Educt1 + Educt 2 + Product). With this formula, 100% conjugation can only be achieved with exactly equimolar educt quantities, because both educt 1 and educt 2 need to be converted entirely. If one educt 1 is available in excess, for example because of protein concentration measurement inaccuracies or pipetting errors, some of it will be left without fusion partner. In case of Figure 3B, 3% more GST seemed to have been in the mixture. These are methodological inaccuracies.
(2) Please provide at least one example of a purified desired product, and mention the difficulties involved as a disadvantage to this particular method. Separating BcPAP, Connectase, and the desired protein-protein conjugate may prove to be quite difficult, especially when Connectase cleaves off affinity tags.
Examples are now provided in Figure 6. As described in the discussion (p. 8, ln 258-264), the simple product purification is one of the advantages of the method.
(3) For the antibody conjugate, please provide an example of conjugating an edduct that would prove to be more useful in the context of antibodies. For example, as you mention in the introduction, conjugation of fluorophores, immobilization tags such as biotin, and small molecule linker/drugs are useful bioconjugates to antibodies.
Antibody-biotinylation is now shown in Figure S6; Antibody-fluorophore conjugates are part of Figures S5 and S7.
(4) Please assess the stability of these protein-protein conjugates under various conditions (temperature, pH, time) to ensure that the ligation via Connectase is stable over a broad array of conditions. In particular, a relevant antibody-conjugate stability assay should be done over the period of 1-week in both buffer and plasma to show applicability for potential therapeutics.
The stability of an antibody-biotin conjugate in blood plasma over 7 days at different temperatures is now shown in Figure S7.
Generally, Connectase introduces a regular peptide bond (Asp-Ala) with a high chemical and physical stability (e.g. 10 min incubation at 95°C in SDS-PAGE loading buffer; H2O-formic acid / acetonitrile gradients for LC-MS). The sequence may be susceptible to proteases, although this is not the case in HEK293 cells (antibody expression), E. coli, or blood plasma (Figure S7).
(5) Please conduct functional assays with the antibody-protein/peptide conjugates to show that the antibody retains binding capabilities to the HER-2 antigen and the modification was site-selective, not interfering with the binding paratope or binding ability of the antibody in any way. This can be done through bio-layer interferometry, surface plasmon resonance, ELISA, etc.
We plan the immobilization of the HER2 antibody on microplates and its use in an ELISA. However, this experiment requires significant testing and optimizations. It will be part of a future paper on the use of Connectase for protein immobilization.
For now, the mass spectrometry data provide clear evidence of a single site-selective conjugation, as the C-terminal ELASKDPGAFDADPLVVEI-Strep sequence is replaced by ELASKDAGAFDADPLVVEI(-Ub). Given that the conjugation sites at the C-termini are far from the antigen binding sites, and have already been used in a number of other approaches (e.g., SpyTag, SnapTag, Sortase), it appears unlikely that these conjugations interfere with antigen binding.
(6) Please include gels of all proteins used in ligation reactions after purification steps in the SI to show that each species was pure.
The pure proteins are now shown in Figure S9.
(7) Please provide the figures (not just tables) of LC/MS deconvoluted mass spectra graphs for all conjugates, either in the main text or the SI.
Please specify which spectra you are missing. I believe all relevant spectra are shown in Figures 4, 5, and S3. The primary data can be found in Dataset S2.
(8) Please provide more information in the methods section on exactly how the densitometry quantification of gel bands was performed with ImageJ.
Details on the quantification with Image Studio Lite 5.2 were added in the method section (p. 17, ln 461-463).
Minor Suggestions:
(1) Page 1, line 19: can include one sentence on what assays these particular bioconjugations are usefule for (e.g. internalization cell studies, binding assays, etc.)
I prefer not to provide additional details here to keep the text concise and focused.
(2) Page 1, line 22: "three to ten equivalents" instead of 3x-10x.
Done.
(3) Page 1, line 23: While NHS labeling is widely considered non-specific, maleimide conjugation to free cysteines is generally considered specific for engineered free cysteine residues, since native proteins often do not have free cysteine residues available for conjugation. If you are referring to the potential of maleimides to label lysines as well, that should be specifically stated.
I modified the sentence, now stating that these methods are "can be" unspecific.
As pointed out, it is possible to achieve specificity by eliminating all other free cysteines and/or engineering a cysteine in an appropriate position. In many other cases, however (e.g., natural antibodies), several cysteines are available, or the sample contains other proteins/peptides. I did not want to go into more detail here and refer to the cited review.
(4) Page 1, line 31: "and an oligoglycine G(1-5)-B"
Done.
(5) Page 1, line 34: It is not clear where in the source these specific Km values are coming from, considering these are variable based on specific conditions/substrates and tend to be reaction-specific.
I cited another review, which lists the same values, along with a few other measurements (Jacobitz et al., Adv Protein Chem Struct Biol 2017, Table 2). It is clear that each of these measurements differs somewhat, but they are generally comparable (K<sub>M</sub>(LPETG) = 5500 - 8760 µM; K<sub>M</sub>(GGGGG) = 140 - 196 µM). I chose the cited study (Frankel et al., Biochemistry 2005), because it also investigated hydrolysis rates. In this study, the measurements are derived from the plots in Figure 2.
(6) Page 1, line 47: the comparison to western blots feels a little like apples to oranges, even though this comparison was made in previous literature. Engineering an expressed protein to have this tag and then using the tag to detect and quantify it, feels more akin to a tagging/pull down assay than a western blot in which unmodified proteins are easily detected.
It is akin to a frequently used type of western blots with tag-specific antiboies, e.g. Anti-His<sub>6</sub>, -Streptavidin, -His<sub>6</sub>, -HA ,-cMyc, -Flag. I modified the sentence to clarify this.
(7) Page 2, line 51: "Connectase cleaves between the first D and P amino acids in the recognition sequence, resulting in an N-terminal A-ELASKD-Connectase intermediate and a C-terminal PGAFDADPLVVEI peptide."
I prefer the current sentence, because we assume that a bond between the aspartate and Connectase is formed before PGAFDADPLVVEI is cleaved off.
(8) Page 3, line 94: "Exact determination is not possible due to reversibility of the reaction", the way it is stated now sounds like it is a flaw in the methods. Also, update Figure 2 to read "Estimated relative ligation rate".
Done.
(9) Page 3, lines 101-107: This is worded in a confusing way. It can either be X<sub>1</sub> or X<sub>2</sub> that is inactivated depending on if the altered amino acid is on the original protein sequence or on the desired edduct to conjugate. You first give examples of how to render other amino acids inactive, but then ultimately state that proline made inactive, so separate the two distinct possibilities a bit more clearly.
The reaction requires the inactivation of X<sub>1</sub>, without affecting X<sub>2</sub> (ln 100 - 102). This is true, no matter whether it is X<sub>1</sub> = A, C, S, or P that is inactivated. I added a sentence to clarify this (ln 102 – 103).
(10) Page 4, line 118: Give a one-sentence justification for why these proteins were chosen to work with (easy to express, stable, etc).
Done.
(11) Page 5, line 167: "payload molecules".
Done.
(12) Page 5, lines 170-173: Word this more clearly- "full conversion with many of these methods is difficult on antibodies due to each heavy and light chain being modified separately, resulting in only a total yield of 66% DAR4 even when 90% of each chain is conjugated."
I rephrased the section.
(13) Page 8, line 290: Discuss other disadvantages of this method including difficulties purifying and in incorporating such a long sequence into proteins of interest.
Product purification is shown in the new Figure 6. As stated above, I consider the simple purification process an advantage of the method. The genetic incorporation of the sequence into proteins is a routine process and should not make any difficulties. The disadvantages of long linker sequences between fusion partners are now discussed (p.8 – 9, ln 300-302).
(14) Page 10, line 341: 'The experiment is described and discussed in detail in a previously published paper.31"
Done.
Reviewer #2 (Recommendations for the authors):
Minor Points:
(1) It's unclear how the author derived 100% ligation rate with X = Proline in Figure 2 when there is still residual unligated UB-Strep at 96h. Please provide an expanded explanation for those not familiar with the protocol. Is the assumption made that there will be no UB-Strep if the assay was carried out beyond 96h?
I clarified the figure legend. The assay shows the formation of an equilibrium between educts and products. Therefore, only ~50% Ub-Strep is used with X = Proline (see p. 2, ln 79 - 81). The "relative ligation rate" refers to the relative speed with which this equilibrium is established. The highest rate is seen with X = Proline, and it is set to 100%. The other rates are given relative to the product formation with X = Proline.
(2) Though the qualitative depiction of the data in Figure 3 is appreciated, an accompanying graphical representation of the data in the same figure will greatly enhance reception and better comprehension of several of the author's conclusions.
Graphs are now shown in Figure S1.
(3) Figure 3 panel E is misaligned. Please align it with panel B above it.
Done, thank you.
(4) The author refers to 'The resulting circular assemblies (37% UB2...)' in the text but identifies it as UB-C2 in Figure 5B. Is this a mistake or does UB2 refer to another assembly not mentioned in the Figures? Please check for inconsistencies.
All circular assemblies are now labeled Ub-C <sub>1-6</sub>.
(5) Finishing with a graphical schematic that depicts the entire protocol in a simple image would be much appreciated and well-received by readers. Including the scheme with A and B proteins, the recognition linkers, the addition of connectase and BcPAP, etc. to the final resulting protein with connected linker.
A graphical summary of the reaction is now included in Figure 6.
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www.biorxiv.org www.biorxiv.org
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Author response:
The following is the authors’ response to the original reviews.
Reviewer #1 (Public review):
Summary:
Chen and Phillips describe the dynamic appearance of cytoplasmic granules during embryogenesis analogous to SIMR germ granules, and distinct from CSR-1-containing granules, in the C. elegans germline. They show that the nuclear Argonaute NRDE-3, when mutated to abrogate small RNA binding, or in specific genetic mutants, partially colocalizes to these granules along with other RNAi factors, such as SIMR-1, ENRI-2, RDE-3, and RRF-1. Furthermore, NRDE-3 RIP-seq analysis in early vs. late embryos is used to conclude that NRDE-3 binds CSR-1-dependent 22G RNAs in early embryos and ERGO-1dependent 22G RNAs in late embryos. These data lead to their model that NRDE-3 undergoes small RNA substrate "switching" that occurs in these embryonic SIMR granules and functions to silence two distinct sets of target transcripts - maternal, CSR-1 targeted mRNAs in early embryos and duplicated genes and repeat elements in late embryos.
Strengths:
The identification and function of small RNA-related granules during embryogenesis is a poorly understood area and this study will provide the impetus for future studies on the identification and potential functional compartmentalization of small RNA pathways and machinery during embryogenesis.
Weaknesses:
(1) While the authors acknowledge the following issue, their finding that loss of SIMR granules has no apparent impact on NRDE-3 small RNA loading puts the functional relevance of these structures into question. As they note in their Discussion, it is entirely possible that these embryonic granules may be "incidental condensates." It would be very welcomed if the authors could include some evidence that these SIMR granules have some function; for example, does the loss of these SIMR granules have an effect on CSR-1 targets in early embryos and ERGO-1-dependent targets in late embryos?
We appreciate reviewer 1’s concern that we do not provide enough evidence for the function of the SIMR granules. As suggested, we examined the NRDE-3 bound small RNAs more deeply, and we do observe a slight but significant increased CSR-class 22G-RNAs binding to NRDE-3 in late embryos of simr-1 and enri-2 mutants (see below, right). We hypothesize that this result could be due to a slower switch from CSR to ERGO 22G-RNAs in the absence of SIMR granules. We added these data to Figure 6G.
(2) The analysis of small RNA class "switching" requires some clarification. The authors re-define ERGO1-dependent targets in this study to arrive at a very limited set of genes and their justification for doing this is not convincing. What happens if the published set of ERGO-1 targets is used?
As we mentioned in the manuscript, we initially attempted to use the previously defined ERGO targets. However, the major concern is fewer than half the genes classified as ERGO targets by Manage et al. and Fischer et al. overlap with one another (Figure 6—figure supplement 1D and below). We reason this might because the gene sets were defined as genes that lose small RNAs in various ERGO pathway mutants and because different criteria were used to define the lists as discussed in the manuscript (lines 471-476). As a result, some of the previously defined ERGO target genes may actually be indirect targets of the pathway. Here we focus on genes targeted by small RNAs enriched in an ERGO pathway Argonaute IP, which should be more specific.
In this manuscript, we are interested specifically in the ERGO targets bound by NRDE-3, thus we utilized the IP-small RNA sequencing data from young adult animals (Seroussi et al, 2023), to define a new ERGO list. We are confident about this list because 1) Most of our new ERGO genes overlap with the overlap between ERGO-Manage and ERGO-Fischer list (see Figure 6—figure supplement 1D in our manuscript and below). 2) We observed the most significant decrease of small RNA levels and increase of mRNA levels in the nrde-3 mutants using our newly defined list (see Figure 6—figure supplement 1E-F in our manuscript).
To further address reviewer 1’s concern about whether the data would look significantly different when using the ERGO-Manage and ERGO-Fischer lists, we made new scatter plots shown in Author response image 1 panels A-C below (ERGO-Manage – purple, ERGO-Fischer- yellow, and the overlap - yellow with purple ring). We found that the small switching pattern of NRDE-3 is consistent with our newly defined list, particularly if we look at the overlap of ERGO-Manage and ERGO-Fischer list (Author response image 1 panels D-F below, red).
Author response image 1.
Further, the NRDE-3 RIP-seq data is used to conclude that NRDE-3 predominantly binds CSR-1 class 22G RNAs in early embryos, while ERGO-1-dependent 22G RNAs are enriched in late embryos. a) The relative ratios of each class of small RNAs are given in terms of unique targets. What is the total abundance of sequenced reads of each class in the NRDE-3 IPs?
To address the reviewer’s question about the total abundance of sequenced reads of each class in the NRDE-3 IPs: Author response image 2 panel A-B below show the total RPM of CSR and ERGO class sRNAs in inputs and IPs at different stages. Focusing on late embryos, the total abundance of ERGO-dependent sRNAs is similar to CSR-class sRNAs in input, while much higher in IP, indicating an enrichment of ERGO-dependent 22G-RNAs in NRDE-3 consistent with our log2FC (IP vs input) in Figure 6B. This data supports our conclusion that NRDE-3 preferentially binds to ERGO targets in late embryos.
Author response image 2.
b) The "switching" model is problematic given that even in late embryos, the majority of 22G RNAs bound by NRDE-3 is the CSR-1 class (Figure 5D).
It is important to keep in mind the difference in the total number of CSR target genes (3834) and ERGO target genes (119). The pie charts shown in Figure 6D are looking at the total proportion of the genes enriched in the NRDE-3 IP that are CSR or ERGO targets. For the NRDE-3 IP in late embryos, that would be 70/119 (58.8%) of ERGO targets are enriched, while 172/3834 (4.5%) of CSR targets are enriched. These data are also supported by the RPM graphs shown in Author response image 2 panels A-B above, which show that the majority of the small RNA bound by NRDE-3 in late embryos are ERGO targets. Nonetheless, NRDE-3 still binds to some CSR targets shown as Figure 6D and panel B, which may be because the amount of CSR-class 22G-RNAs is reduced gradually across embryonic development as the maternally-deposited NRDE-3 loaded with CSR-class 22G-RNAs is diluted by newly transcribed NRDE-3 loaded with ERGOdependent 22G-RNAs (lines 857-862).
c) A major difference between NRDE-3 small RNA binding in eri-1 and simr-1 mutants appears to be that NRDE-3 robustly binds CSR-1 22G RNAs in eri-1 but not in simr-1 in late embryos. This result should be better discussed.
In the eri-1 mutant, we hypothesize that NRDE-3 robustly binds CSR-class 22G-RNAs because ERGOclass 22G-RNAs are not synthesized during mid-embryogenesis, so either NRDE-3 is unloaded (in granule at 100-cell stage in Figure 2A) or mis-loaded with CSR-class 22G-RNAs (in the nucleus at 100cell stage in Figure 2A). We don’t have a robust method to address the proportion of loaded vs. unloaded NRDE-3 so it is difficult to address the degree to which NRDE-3 is misloaded in the eri-1 mutant. In the simr-1 mutant, both classes of small RNAs are present and NRDE-3 is still preferentially loaded with ERGO-dependent 22G-RNAs, though we do see a subtle increase in association with CSR-class 22GRNAs. These data could suggest a less efficient loading of NRDE-3 with ERGO-dependent 22G-RNAs, but we would need more precise methods to address the loading dynamics in the simr-1 mutant.
(3) Ultimately, if the switching is functionally important, then its impact should be observed in the expression of their targets. RNA-seq or RT-qPCR of select CSR-1 and ERGO-1 targets should be assessed in nrde-3 mutants during early vs late embryogenesis.
The function of NRDE-3 at ERGO targets has been well studied (Guang et al, 2008) and is also assessed in our H3K9me3 ChIP-seq analysis in Figure 7E where, in mixed staged embryos, H3K9me3 level on ERGO targets (labeled as ‘NRDE-3 targets in young adults’) is reduced significantly in the nrde-3 mutant.
To understand the function of NRDE-3 binding on CSR targets in early embryos, we attempted to do RTqPCR, smFISH, and anti-H3K9me3 CUT&Tag-seq on early embryos, and we either failed to obtain enough signal or failed to detect any significant difference (data not shown). We additionally tested the possibility that NRDE-3 functions with CSR-class 22G-RNAs in oocytes. We present new data showing that NRDE-3 represses RNA Pol II in oocytes to promote global transcriptional repression at the oocyteto-embryo transition, we now included these data in Figure 8.
Reviewer #2 (Public review):
Summary:
NRDE-3 is a nuclear WAGO-clade Argonaute that, in somatic cells, binds small RNAs amplified in response to the ERGO-class 26G RNAs that target repetitive sequences. This manuscript reports that, in the germline and early embryos, NRDE-3 interacts with a different set of small RNAs that target mRNAs. This class of small RNAs was previously shown to bind to a different WAGO-clade Argonaute called CSR1, which is cytoplasmic, unlike nuclear NRDE-3. The switch in NRDE-3 specificity parallels recent findings in Ascaris where the Ascaris NRDE homolog was shown to switch from sRNAs that target repetitive sequences to CSR-class sRNAs that target mRNAs.
The manuscript also correlates the change in NRDE-3 specificity with the appearance in embryos of cytoplasmic condensates that accumulate SIMR-1, a scaffolding protein that the authors previously implicated in sRNA loading for a different nuclear Argonaute HRDE-1. By analogy, and through a set of corelative evidence, the authors argue that SIMR foci arise in embryogenesis to facilitate the change in NRDE-3 small RNA repertoire. The paper presents lots of data that beautifully documents the appearance and composition of the embryonic SIMR-1 foci, including evidence that a mutated NRDE-3 that cannot bind sRNAs accumulates in SIMR-1 foci in a SIMR-1-dependent fashion.
Weaknesses:
The genetic evidence, however, does not support a requirement for SIMR-1 foci: the authors detected no defect in NRDE-3 sRNA loading in simr-1 mutants. Although the authors acknowledge this negative result in the discussion, they still argue for a model (Figure 7) that is not supported by genetic data. My main suggestion is that the authors give equal consideration to other models - see below for specifics.
We appreciate reviewer 2’s comments on the genetic evidence for the function of SIMR foci. A similar concern was also brought up by reviewer 1. By re-examining our sequencing data, we found that there is a modest but significant increase in NRDE-3 association with CSR-class sRNAs in simr-1 and enri-2 mutants in late embryos. We believe that this data supports our model that SIMR-1 and ENRI-2 are required for an efficient switch of NRDE-3 bound small RNAs. Please refer our response to the reviewer 1 - point (1), and Figure 6G in the updated manuscript.
Reviewer #3 (Public review):
Summary:
Chen and Phillips present intriguing work that extends our view on the C. elegans small RNA network significantly. While the precise findings are rather C. elegans specific there are also messages for the broader field, most notably the switching of small RNA populations bound to an argonaute, and RNA granules behavior depending on developmental stage. The work also starts to shed more light on the still poorly understood role of the CSR-1 argonaute protein and supports its role in the decay of maternal transcripts. Overall, the work is of excellent quality, and the messages have a significant impact.
Strengths:
Compelling evidence for major shift in activities of an argonaute protein during development, and implications for how small RNAs affect early development. Very balanced and thoughtful discussion.
Weaknesses:
Claims on col-localization of specific 'granules' are not well supported by quantitative data
We have now included zoomed images of individual granules to better show the colocalization in Figure 4 and Figure 4—figure supplement 1, and performed Pearson’s colocalization analysis between different sets of proteins in Figure 4B.
Reviewer #2 (Recommendations for the authors):
- The manuscript is very dense and the gene names are not helpful. For example, the authors mention ERGO-1 without clarifying the type of protein, etc. I suggest the authors include a figure to go with the introduction that describes the different classes of primary and secondary sRNAs, associated Argonautes, and other accessory proteins. Also include a table listing relevant gene names, protein classes, main localizations, and proposed functions for easy reference by the readers.
We agree that the genes names in different small RNA pathways are easily confused. We added a diagram and table in Figure 1—figure supplement 1 depicting the ERGO/NRDE and CSR pathways and added clarification about the ERGO/NRDE-3 pathway in the text from line 126-128.
- Line 424 - the wording here and elsewhere seems to imply that SIMR-1 and ENRI-2, although not essential, contribute to NRDE-3 sRNA loading. The sequencing data, however, do not support this - the authors should be clearer on this. If the authors believe there are subtle but significant differences, they should show them perhaps by adding a panel in Figure 5 that directly compares the NRDE-3 IPs in wildtype versus simr-1 mutants. Figure 5H however does not support such a requirement.
As brought up by reviewer 1, we do not see difference in binding of ERGO-dependent sRNA in simr-1 mutant in late embryos. We do, however, see a modest, but significant, increase of CSR-sRNAs bound by NRDE-3 in simr-1 and enri-2 mutants, which we hypothesize could be due to a less efficient loading of ERGO-dependent 22G-RNAs by NRDE-3. The updated data are now in Figure 6G. We have also edited the text and model figure to soften these conclusions.
- Condensates of PGL proteins appear at a similar time and place (somatic cells of early embryos) as the embryonic SIMR-1 foci. The PGL foci correspond to autophagy bodies that degrade PGL proteins. Is it possible that SIMR-1 foci also correspond to degradative structures? The possibility that SIMR-1 foci are targeted for autophagy and not functional would fit with the finding that simr-1 mutants do not affect NRDE-3 loading in embryos.
We appreciate reviewer 2’s comments on possibility of SIMR granules acting as sites for degradation of SIMR-1 and NRDE-3. We think this is not the case for the following reasons: 1) if SIMR granules are sites of autophagic degradation, then we would expect that embryonic SIMR granules in somatic cells, like PGL granules, should only be observed in autophagy mutants; however we see them in wild-type embryos 2) we would not expect a functional Tudor domain to be required for granule localization; however in Figure 1—figure supplement 2B, we show that a point mutation in the Tudor domain of SIMR-1 abrogates SIMR granule formation, and 3) if NRDE-3(HK-AA) is recruited to SIMR granules for degradation while wild-type NRDE-3 is cytoplasmic, then NRDE-3(HK-AA) should shows a significantly reduced protein level comparing to wild-type NRDE-3. In the western blot in Figure 2—figure supplement 1B, NRDE-3 and NRDE-3(HK-AA) protein levels are similar, indicating that NRDE-3(HK-AA) is not degraded despite being unloaded. This is in contrast to what we have observed previously for HRDE-1, which is degraded in its unloaded state. If SIMR-1 played a role directly in promoting degradation of NRDE-3(HK-AA), we would similarly expect to see a change in NRDE-3 or NRDE-3(HK-AA) expression in a simr-1 mutant. We performed western blot and did not observe a significant change in protein expression for NRDE-3 (Figure 3—figure supplement 1A).
Although under wild-type conditions, SIMR granules do not appear to be sites of autophagic degradation, upon treatment with lgg-1 (an autophagy protein) RNAi, we found that SIMR-1, as well as many other germ granule and embryonic granule-localized proteins, increase in abundance in late embryos. This data demonstrates that ZNFX-1, CSR-1, SIMR-1, MUT-2/RDE-3, RRF-1, and unloaded NRDE-3 are removed by autophagic degradation similar to what have been shown previously for PGL-1 proteins (Zhang et al, 2009, Cell). We added these data to Figure 5. It is important to emphasize, however, that the timing of degradation differs for each granule assayed (Lines 447-450), indicating that there must be multiple waves of autophagy to selectively degrade subsets of proteins when they are no longer needed by the embryo.
- The observation that an NRDE-3 mutant that cannot load sRNAs localizes to SIMR-1 foci does not necessarily imply that wild-type unloaded NRDE-3 would also localize there. Unless the authors have additional data to support this idea, the authors should acknowledge that this hypothesis is speculative. In fact, why does cytoplasmic NRDE-3 not localize to granules in the rde-3;ego-1degron strain shown in Figure 6B?? Is it possible that the NRDE-3 mutant accumulates in SIMR-1 foci because it is unfolded and needs to be degraded?
We believe that wild-type NRDE-3 also localize to SIMR foci when unloaded. This is supported by the localization of wild-type NRDE-3 in eri-1 and rde-3 mutants, where a subset of small RNAs are depleted. Wild-type NRDE-3 localizes to both somatic SIMR-1 granules and the nucleus, depending on embryo stage (Figure 2A, Figure 2—figure supplement 1C). The granule numbers in eri-1 and rde-3 mutants are less than the nrde-3(HK-AA) mutant, consistent with the imaging data that NRDE-3 only partially localize to somatic granule (Figure 2A – 100-cell stage).
In the rde-3; ego-1 double mutant, the embryos have severe developmental defect: they cannot divide properly after 4-8 cell stage and exhibit morphology defects after that stage. In wild-type, SIMR foci does not appear until around 8-28-cell stage (shown in Figure 1C), so we believe that cytoplasmic NRDE-3 does not localize to foci in the double mutant is because of the timing.
- The authors propose that NRDE-3 functions in nuclei to target mRNAs also targeted in the cytoplasm by CSR-1. If so, how do they propose that NRDE-3 might do this since little transcription occurs in oocytes/early embryos?? Are the authors suggesting that NRDE-3 targets germline genes for silencing specifically at the times that zygotic transcription comes back on, or already in maturing oocytes? Is the transcription of most CSR-1 targets silenced in early embryos??
We appreciate the suggestions to check the function of NRDE-3 in oocytes. We tested this possibility and found it to be correct. NRDE-3 functions in oocytes for transcriptional repression by inhibiting RNA Pol II elongation. We added these data to Figure 8. We also attempted to do RT-qPCR, smFISH, and antiH3K9me3 Cut&Tag-seq on early embryos to further test the hypothesis that NRDE-3 acts with CSR-class 22G-RNAs in early embryos, but we either failed to obtain enough signal or failed to detect any significant difference (data not shown). Therefore, we think that the primary role for NRDE-3 bound to CSR-class 22G-RNAs may be for global transcriptional repression of oocytes prior to fertilization.
- Line 684-686: "In summary, this work investigating the role of SIMR granules in embryos, together with our previous study of SIMR foci in the germline (Chen and Phillips 2024), has identified a new mechanism for small RNA loading of nuclear Argonaute proteins in C. elegans". This statement appears overstated/incorrect since there is no evidence that SIMR-1 foci are required for sRNA loading of NRDE3. The authors should emphasize other models, as suggested above.
We have revised the text on line 869-871 to emphasize that SIMR granule regulate the localization of nuclear Argonaute proteins, rather than suggesting a direct role on controlling small RNA loading. We also edit the title, text, and legend for our model in Figure 9.
Reviewer #3 (Recommendations for the authors):
Issues to be addressed:
- The authors show a switch in 22G RNA binding by NRDE-3 during embryogenesis. While the data is convincing, it would be great if it could be tested if the preferred NRDE-3 replacement model is indeed correct. This could be done relatively easily by giving NRDE-3 a Dendra tag, allowing one to colour-switch the maternal WAGO-3 pool before the zygotic pool comes up. Such data would significantly enhance the manuscript, as this would allow the authors to follow the fate of maternal NRDE-3 more precisely, perhaps identifying a period of sharp decline of maternal NRDE-3.
We think the NRDE-3 Dendra tag experiment suggested by the reviewer is a clever approach and we will consider generating this strain in the future. However, we feel that optimization of the color-switching tag between the maternal germline and the developing embryos is beyond the scope of this manuscript. To partially address the question about NRDE-3 fate during embryogenesis, we examined the single-cell sequencing data of C. elegans embryos from 1-cell to 16-cell stage (Tintori et al, 2016, Dev Cell; Visualization tool from John I Murray lab), as shown in Author response image 3 Panel A below, NRDE-3 transcript level increases as embryo develops, indicating that zygotic NRDE-3 is being actively expressed starting very early in development. We hypothesize that maternal NRDE-3 will either be diluted as the embryo develops or actively degraded during early embryogenesis.
Author response image 3.
- Figure 3A: * should mark PGCs, but this seems incorrect. At the 8-cell stage there still is only one PGC (P4), not two, and at 100 cells there are only two, not three germ cells. Also, the identification of PGCs with a maker (PGL for instance) would be much more convincing.
We apologize for the confusion in Figure 3A. We changed the figure legend to clarify that the * indicate nuclear NRDE-3 localization in somatic cells for 8- and 100-cell stage embryos rather than the germ cells.
- Overall, the authors should address colocalization more robustly. In the current manuscript, just one image is provided, and often rather zoomed-out. How robust are the claims on colocalization, or lack thereof? With the current data, this cannot be assessed. Pearson correlation, combined with line-scans through a multitude of granules in different embryos will be required to make strong claims on colocalization. This applies to all figures (main and supplement) where claims on different granules are derived from.
We thank reviewer 3 for this important suggestion. To better address the colocalization, we included insets of individual granules in Figure 2D and Figure 4. We also performed colocalization analysis by calculating the Pearson’s R value between different groups of proteins in Figure 4B, to highlight that SIMR-1 colocalizes with ENRI-2, NRDE-3(HK-AA), RDE-3, and RRF-1, while CSR-1 colocalizes with EGO-1.
For the proteins that lack colocalization in Figure 4—figure supplement 1, we also added insets of individual granules. Additionally, we included a new set of panels showing SIMR-1 localization compared to tubulin::GFP (Figure 4—figure supplement 1I) in response to a recent preprint (Jin et al, 2024, BioRxiv), which finds NRDE-3 (expressed under a mex-5 promoter) associating with pericentrosomal foci and the spindle in early embryos. We do not see SIMR-1 (or NRDE-3, data not shown) at centrosomes or spindles in wild-type conditions but made a similar observation for SIMR-1 in a mut-16 mutant (Figure 4E). All of the localization patterns were examined on at least 5 individual 100-cell staged embryos with same localization pattern.
- Figure 7: Its title is: Function of cytoplasmic granules. This is a much stronger statement than provided in the nicely balanced discussion. The role of the granules remains unclear, and they may well be just a reflection of activity, not a driver. While this is nicely discussed in the text, figure 7 misses this nuance. For instance, the title suggests function, and also the legend uses phrases like 'recruited to granule X'. If granules are the results of activity, 'recruitment' is really not the right way to express the findings. The nuance that is so nicely worded in the discussion should come out fully in this figure and its legend as well.
We have changed the title of Figure 7 (now Figure 9) to “Model for temporally- and developmentallyregulated NRDE-3 function” to deemphasize the role of the granules and to highlight the different functions of NRDE-3. Similarly, we have rephrased the text in the figure and legend and add a some details about our new results.
Minor:
Typo: line 663 Acaris
We corrected the typo.
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www.biorxiv.org www.biorxiv.org
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Author response:
The following is the authors’ response to the previous reviews.
Reviewer #2:
(1) The use of two m<sup>5</sup>C reader proteins is likely a reason for the high number of edits introduced by the DRAM-Seq method. Both ALYREF and YBX1 are ubiquitous proteins with multiple roles in RNA metabolism including splicing and mRNA export. It is reasonable to assume that both ALYREF and YBX1 bind to many mRNAs that do not contain m<sup>5</sup>C.
To substantiate the author's claim that ALYREF or YBX1 binds m<sup>5</sup>C-modified RNAs to an extent that would allow distinguishing its binding to non-modified RNAs from binding to m<sup>5</sup>C-modified RNAs, it would be recommended to provide data on the affinity of these, supposedly proven, m<sup>5</sup>C readers to non-modified versus m<sup>5</sup>C-modified RNAs. To do so, this reviewer suggests performing experiments as described in Slama et al., 2020 (doi: 10.1016/j.ymeth.2018.10.020). However, using dot blots like in so many published studies to show modification of a specific antibody or protein binding, is insufficient as an argument because no antibody, nor protein, encounters nanograms to micrograms of a specific RNA identity in a cell. This issue remains a major caveat in all studies using so-called RNA modification reader proteins as bait for detecting RNA modifications in epitranscriptomics research. It becomes a pertinent problem if used as a platform for base editing similar to the work presented in this manuscript.
The authors have tried to address the point made by this reviewer. However, rather than performing an experiment with recombinant ALYREF-fusions and m<sup>5</sup>C-modified to unmodified RNA oligos for testing the enrichment factor of ALYREF in vitro, the authors resorted to citing two manuscripts. One manuscript is cited by everybody when it comes to ALYREF as m<sup>5</sup>C reader, however none of the experiments have been repeated by another laboratory. The other manuscript is reporting on YBX1 binding to m<sup>5</sup>C-containing RNA and mentions PAR-CLiP experiments with ALYREF, the details of which are nowhere to be found in doi: 10.1038/s41556-019-0361-y.<br /> Furthermore, the authors have added RNA pull-down assays that should substitute for the requested experiments. Interestingly, Figure S1E shows that ALYREF binds equally well to unmodified and m<sup>5</sup>C-modified RNA oligos, which contradicts doi:10.1038/cr.2017.55, and supports the conclusion that wild-type ALYREF is not specific m<sup>5</sup>C binder. The necessity of including always an overexpression of ALYREF-mut in parallel DRAM experiments, makes the developed method better controlled but not easy to handle (expression differences of the plasmid-driven proteins etc.)
Thank you for pointing this out. First, we would like to correct our previous response: the binding ability of ALYREF to m<sup>5</sup>C-modified RNA was initially reported in doi: 10.1038/cr.2017.55, (and not in doi: 10.1038/s41556-019-0361-y), where it was observed through PAR-CLIP analysis that the K171 mutation weakens its binding affinity to m<sup>5</sup>C -modified RNA.
Our previous experimental approach was not optimal: the protein concentration in the INPUT group was too high, leading to overexposure in the experimental group. Additionally, we did not conduct a quantitative analysis of the results at that time. In response to your suggestion, we performed RNA pull-down experiments with YBX1 and ALYREF, rather than with the pan-DRAM protein, to better validate and reproduce the previously reported findings. Our quantitative analysis revealed that both ALYREF and YBX1 exhibit a stronger affinity for m<sup>5</sup>C -modified RNAs. Furthermore, mutating the key amino acids involved in m<sup>5</sup>C recognition significantly reduced the binding affinity of both readers. These results align with previous studies (doi: 10.1038/cr.2017.55 and doi: 10.1038/s41556-019-0361-y), confirming that ALYREF and YBX1 are specific readers of m<sup>5</sup>C -modified RNAs. However, our detection system has certain limitations. Despite mutating the critical amino acids, both readers retained a weak binding affinity for m<sup>5</sup>C, suggesting that while the mutation helps reduce false positives, it is still challenging to precisely map the distribution of m<sup>5</sup>C modifications. To address this, we plan to further investigate the protein structure and function to obtain a more accurate m<sup>5</sup>C sequencing of the transcriptome in future studies. Accordingly, we have updated our results and conclusions in lines 294-299 and discuss these limitations in lines 109-114.
In addition, while the m<sup>5</sup>C assay can be performed using only the DRAM system alone, comparing it with the DRAM<sup>mut</sup>C control enhances the accuracy of m<sup>5</sup>C region detection. To minimize the variations in transfection efficiency across experimental groups, it is recommended to use the same batch of transfections. This approach not only ensures more consistent results but also improve the standardization of the DRAM assay, as discussed in the section added on line 308-312.
(2) Using sodium arsenite treatment of cells as a means to change the m<sup>5</sup>C status of transcripts through the downregulation of the two major m<sup>5</sup>C writer proteins NSUN2 and NSUN6 is problematic and the conclusions from these experiments are not warranted. Sodium arsenite is a chemical that poisons every protein containing thiol groups. Not only do NSUN proteins contain cysteines but also the base editor fusion proteins. Arsenite will inactivate these proteins, hence the editing frequency will drop, as observed in the experiments shown in Figure 5, which the authors explain with fewer m<sup>5</sup>C sites to be detected by the fusion proteins.
The authors have not addressed the point made by this reviewer. Instead the authors state that they have not addressed that possibility. They claim that they have revised the results section, but this reviewer can only see the point raised in the conclusions. An experiment would have been to purify base editors via the HA tag and then perform some kind of binding/editing assay in vitro before and after arsenite treatment of cells.
We appreciate the reviewer’s insightful comment. We fully agree with the concern raised. In the original manuscript, our intention was to use sodium arsenite treatment to downregulate NSUN mediated m<sup>5</sup>C levels and subsequently decrease DRAM editing efficiency, with the aim of monitoring m<sup>5</sup>C dynamics through the DRAM system. However, as the reviewer pointed out, sodium arsenite may inactivate both NSUN proteins and the base editor fusion proteins, and any such inactivation would likely result in a reduced DRAM editing. This confounds the interpretation of our experimental data.
As demonstrated in Appendix A, western blot analysis confirmed that sodium arsenite indeed decreased the expression of fusion proteins. In addition, we attempted in vitro fusion protein purification using multiple fusion tags (HIS, GST, HA, MBP) for DRAM fusion protein expression, but unfortunately, we were unable to obtain purified proteins. However, using the Promega TNT T7 Rapid Coupled In Vitro Transcription/Translation Kit, we successfully purified the DRAM protein (Appendix B). Despite this success, subsequent in vitro deamination experiments did not yield the expected mutation results (Appendix C), indicating that further optimization is required. This issue is further discussed in line 314-315.
Taken together, the above evidence supports that the experiment of sodium arsenite treatment was confusing and we determined to remove the corresponding results from the main text of the revised manuscript.
Author response image 1.
(3) The authors should move high-confidence editing site data contained in Supplementary Tables 2 and 3 into one of the main Figures to substantiate what is discussed in Figure 4A. However, the data needs to be visualized in another way then excel format. Furthermore, Supplementary Table 2 does not contain a description of the columns, while Supplementary Table 3 contains a single row with letters and numbers.
The authors have not addressed the point made by this reviewer. Figure 3F shows the screening process for DRAM-seq assays and principles for screening high-confidence genes rather than the data contained in Supplementary Tables 2 and 3 of the former version of this manuscript.
Thank you for your valuable suggestion. We have visualized the data from Supplementary Tables 2 and 3 in Figure 4A as a circlize diagram (described in lines 213-216), illustrating the distribution of mutation sites detected by the DRAM system across each chromosome. Additionally, to improve the presentation and clarity of the data, we have revised Supplementary Tables 2 and 3 by adding column descriptions, merging the DRAM-ABE and DRAM-CBE sites, and including overlapping m<sup>5</sup>C genes from previous datasets.
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