- Aug 2021
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Referee #2
Evidence, reproducibility and clarity
This work describes interesting approach for mapping interactome of specifically modified histone protein using antibody-based APEX2. Although it contains interesting results and useful techniques for biological community, I found that it requires revision and addition for the publication.
- I could understand the reason using antibody-based proximity labeling approach for mapping the biomolecules that interact with post-translationally modified histone becuase it should be complicated to map it with exogenous protein expression approach. However, the introduction of antibody-conjugated APEX2 should require fixation and permeabilization steps that can usually compromise ultrastructure. The authors should comment whether these procedures can affect protein composition and structures of nucleosome in the Discussion part of this manuscript.
2. For generation of biotin-phenoxyl radical, HRP-conjugated antibody can be utilized as shown in BAR method (Daniel Z Bar et al. Nat Methods, 2018, 15, 127-133). Since secondary-HRP antibody is commercially available, one cannot make an effort to express and purify pA-APEX2 for this approach. The autrhos should clearly explain why they selected APEX2 and what is an expected advance(s) using APEX2 in their approach.
3. For the detection of the APEX-mediated biotinylated proteins, direct mass identification of tyrosine-modified peptides with chemical probes can tell the most correct information of the proximal proteins (see Lee SY et al. J. Am. Chem. Soc. 2017, 139, 3651-3662; Namrata D Udeshi et al. Nature Methods 2017, 14, 1167-1170). Thus, if the authors can obtain the biotin-modified peptide information from each antibody-conjugated APEX2, the quality of their interactome results should be much improved. If authors may be under the situation that cannot conduct further mass experiments, it might be required to check whether their important finding molecules (e.g. Arid2, Brd7, Nsd2) are really "biotinylated" by conducting Streptavidin-HRP western blot experiment after enrichment of those proteins by using primary antibody. If biotinylation is specifically conducted by pA-APEX2 with H3K27me3 antibody, the authors can observe SA-HRP blot signal on the enriched protein band on the membrane. Negative controls should be the samples omit pA-APEX2, H3K27me3 antibody, biotin-phenol, H2O2, respectively or using different PTM targeted primary antibody. This result can confirm that their findings are enriched from proximity-dependent biotinylation of APEX2, not from spurious binding events to the other biotinylated proteins or self-labeled bait proteins.
Significance
For antibody-binding APEX2 strategy, this work is not the first one and the authors should mention the precedent work in the manuscript: Jisu Lee et al. Chem. Commun., 2015, 51, 10945-10948. And the author also commented the antibody-based proximity labeling mapping works including Daniel Z Bar et al. Nat Methods, 2018, 15, 127-133 in the manuscript.
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Referee #1
Evidence, reproducibility and clarity
Summary:
In this article, Li and colleagues demonstrate the utility of a novel proximity labeling-based strategy, which they term AMAPEX (antibody-mediated protein A APEX) for the proteomic characterization of the protein environment of specific histone modifications. They apply this new methodology in mouse embryonic fibroblasts for subsequent purification of biotinylated proteins and mass-spectrometric identification.
Major comments:
• The authors present a high quality, descriptive manuscript that introduces a novel proximity labeling approach from a mostly technical point of view. The presentation of the data and methods are mostly clear, such that they should be easy to reproduce.
• The biggest shortcoming of the study in its current form seems to be the lack of a proper assessment of the method's sensitivity AND -most importantly also- specificity. The authors do not validate potentially new interactors of the modified histones experimentally, which would highlight their technology as a discovery tool. Without the assessment of newly identified proteins, these could simply represent false positives, which would point towards an additional requirement for optimization of the experimental setups. In that light the newly identified proteins are merely potential histone interactors. Validation would require establishment or purchase of additional antibodies, or alternatively cloning and transfection of respective candidates, which will probably take an extra 2-3 months of work. While the study may be publishable in its current form, this validation seems a valuable investment to strengthen the preliminary conclusions.
• With two biological replicates the study fulfills the minimum requirements for reproducibility, however, it would benefit from an additional replicate.
Minor point:
• The sentences in lines 22f (and 44f) could be misunderstood. Please rephrase statements to be unambiguous that it specifies the proteomic surrounding of post-translationally modified proteins. The proximity labeling technologies may themselves be limited in identifying post-translationally modified proteins, as they label reactive side-chains that are often targeted by PTMs. Post-translationally modified lysine residues cannot be targeted by biotin ligase-based methodologies, as tyrosine phosphorylations cannot be assessed by peroxidase-based labeling.
Significance
• From a technical point of view, most of the key conclusions of this paper are convincing. Assessing the proteomic environment of post-translationally modified proteins is of extremely high interest and the methodology seems broadly applicable to address such questions. It should be noted that proximity labeling has not originally been utilized to map protein-protein interactions, as the enzymatic activities available probe their surroundings, this could be an over-interpretation. Nonetheless, the "proteomic surrounding" of target proteins, which would also include hard to identify transient interactions is of high general interest for molecular biologists.
• Although it can be generally agreed that having to express an exogenous fusion protein is a limitation of current proximity labeling setups, the methodology presented here in turn has the limitation that it cannot be performed in living cells, which is a significant disadvantage.
• My lab is establishing and constantly improving various proximity labeling methodologies in combination with mass spectrometry for sub-organellar proteomics. While the technology is sound and well executed, I am not an expert in the biology of histone modifications and the proteins involved and cannot assess the novelty nor the actual value of the generated datasets. It appears to me though that additional validation by independent experiments would strengthen the manuscript. The authors describe the usefulness of the technology mainly in confirming known interactors of modified histones, however, it would be nice (for non-specialists) to explicitly state how high the coverage of the known interactors is and discuss why some of them might have been missed.
• The manuscript in its current form completely lacks a discussion of the presented data. Even if the focus will remain on the technical aspects, the findings should be properly discussed by comparison to other proteomics approaches studying histones. Ideally the data should also be discussed in the light of current proximity labeling technologies and potential future directions.
• While I cannot assess the value for histone research, the manuscript will be very interesting for experts focusing on proximity labeling technologies and subcellular proteomics.
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- Jul 2021
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Reply to the reviewers
Dear reviewers,
We thank all reviewers for and their appreciation of our work and even more so for their constructive comments and suggestions, which will significantly improve the quality of the manuscript. We were able to complete the revision and address all reviewer comments. Aside a more stringent discussion of the literature, and rewording of certain paragraphs for clarity, we also generated additional experimental data.
More importantly, to address the concern that we did not provide a positive marker for the intranuclear compartment, we present new images. We attempted to label gamma-Tubulin by generating new antibodies, GFP-tagged strains, and trying multiple commercial antibodies since the beginning of the project. Only recently we found an antibody providing a more specific signal at the expected location, although with some likely cross-reactivity with alpha- and beta-tubulin, and now show these data in the supplements. Additionally, we generated expansion microscopy samples stained with a fluorophore-coupled NHS-Ester, a bulk protein label. These data show that the centrosome contains an exceptionally protein dense hourglass-shaped region, which spans from the extranuclear to the intranuclear compartment, as revealed by centrin and tubulin co-staining. This fortifies our claims about the distinct nature of the intranuclear centrosome compartment containing the microtubule nucleation sites.
Further, we add images of 5-SiR-Hoechst, SPY555-Tubulin, Centrin1-GFP triple labelling live cells to demonstrate the specificity of the microtubule dye and to underline that we are indeed acquiring the dynamics from the first nuclear division on.
In terms of formatting we added line numbers and uploaded high quality figures separately. Due to the added data and panels we needed to split Fig. 1 into two separate figures, rewrote the figure legends and moved them to the end of the document.
Please find below a point-by-point response to the comments.
Best regards,
Julien Guizetti
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
The manuscript by Simon and collaborators addresses the dynamic changes of spindle and hemi-spindle microtubules occurring along schizogony in Plasmodium falciparum. The work explores the temporal correlation of the changes observed in intranuclear spindles with changes at the level of the centriolar plaque; the nuclear microtubule organizing center of these parasites, using centrin as a bona fide marker of the structure. The study shows that spindle microtubules organize from an intranuclear region, devoid of chromatin, distinct from the centrin region which had not been observed or described before. It further shows that centrin does not localize at the nuclear envelope, but it is actually extranuclear.
This work significantly expands on previous knowledge regarding the functional and spatial organization of the nucleus in P. falciparum, and the structure once defined as "an electron dense mass on the nuclear envelope." It uses state of the art microscopy approaches such as STED, UExM and CLEM, in combination with immunolabeling, dyes and parasites over expressing fluorescent protein fusions, to address these questions.
**Major comments:**
- Are the key conclusions convincing?
I find the manuscript successfully addresses the posed questions. The data presented supports the conclusions.
Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?
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.
No
- 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.
N/A
- 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
**Minor comments:**
- Specific experimental issues that are easily addressable.
On the data shown in Figure 1, it is unclear to me what elements are taken into account to define "anaphase." Anaphase could be defined by using chromatin markers - such as CenH3- which have been identified in Plasmodium and the authors make use of in Figure 1F.
We acknowledge that the term anaphase is ill-defined here. Further it suggests a mitotic morphology analogous to the one observed in “classical” models (prophase, metaphase, anaphase,…), which is not fully appropriate. In line with the comments by Reviewer 3 we, therefore, decided to use the term “extended spindle” instead (Fig. 1 & 2). This better reflects the morphological criterion on which we based the stage definition.
- Are prior studies referenced appropriately?
The authors state that "with the exception of centrins and gamma tubulins" few canonical centrosome components are conserved in Plasmodium. These parasites are in fact able to assemble a more or less canonical centriole for microgamete basal body formation. Widely conserved centriolar components such as Sas6 are coded by the malaria genome, and have been characterized previously. This work is neither referenced nor discussed in the manuscript.
The reviewer is right to point out this omission. We were too much focussed on the blood stage centriolar plaques while writing this section, where centrioles are not observed. Of course centriole-like structures are relevant in other life cycle stages, such as microgametes, and should be discussed (line 104). Some previous attempts to endogenously tag Sas6 to verify its localization in blood stages were unfortunately not successful.
- Are the text and figures clear and accurate?
I find the timings shown in Figure 1A, with respect to the schematic quantification shown in Figure 1B, confusing. Shown as it is, one naturally correlates the images on Fig1A above with the cell cycle progression timing shown on Fig1B, below. However, by time 260min, for example, two somewhat adjacent centrin signals can be observed. Though this is defined as anaphase- by an unspecified criterium- this could very well be representative of metaphase. Nonetheless, the timing shown on Figure 1B for "anaphase" onset is 170min, which is inconsistent with the images above. I suggest that either, the quantification is shown in a different format (ex. bar plots) which could then better reflect the cell to cell variations observed (by use of error bars, for example) or that the figure explanation in the results section clarifies this issue.
We understand how this representation is misleading and have adjusted the figure and text accordingly. We modified the time stamps in Fig. 1A (now Fig. 1C) to the scale used in Fig. 1B (now Fig. 1D) i.e. collapse of the hemispindle is t=0 and explain this in the text (line 158). Since we feel that Fig. 1B (now Fig. 1D) is a good and compact visual representation of progression through the first division we kept the bar plots in the supplements (Fig. S1), but added a title clarifying that average duration between multiple movies are shown.
As presented, the data in Figure 1C is rather uninformative. A pattern could be more immediately extracted if dots corresponding to subsequent appearance of centrin dots in the same nucleus were connected to each other.
Concerning the appearance of the centrin signals we adopted the good suggestion by the reviewer and connected “paired” centrin signals by lines (Fig. 1E).
- Do you have suggestions that would help the authors improve the presentation of their data and conclusions?
There are a number of edits required on the text. Row numbers would have been helpful in pointing these out. I point some edits below, but thorough revision of the manuscript for grammatical and synthetic errors would be beneficial.
Cytokinetic segmeter - please replace with "segmented"
Please refer to Figure 1D when appropriate - there is quite an extensive paragraph describing the results shown on this figure, but it is only referenced at the start.
"..., as did the and the number of branches per nucleus,..." please rewrite as appropriate.
We apologize for not providing line numbers, but have corrected the addressed points and applied a grammatical check throughout the manuscript. We have added additional references to Figure 1D (now Fig. 2A) in the text.
Reviewer #1 (Significance (Required)):
This manuscript could be interested to a wide audience interested in cell cycle, cell division, cell organization and organelle positioning, infectious diseases and microscopy. However, the introduction assumes that readers are somewhat experts in the malaria field. I suggest the authors include a brief introduction of the malaria life cycle, and a schematic representation of the division mode. This will help non-experts follow the narrative more easily.
We are happy to read that the reviewer sees value of this study for a broader audience. Following the suggestion, we added a small schematic (Fig. 1A, lines 54, 62) highlighting the relevant steps of schizogony and expanded the introduction of the life cycle (line 46).
This work rectifies long-standing inconsistencies observed by different experimental approaches in the nuclear organization of malaria parasites during schizogony. However, what the functional consequences of the alternative modes of spindle organization in malaria could be, are not clearly stated or discussed. In this respect, as it stands, the manuscript is rather descriptive and lacks mechanistic insight. Nonetheless, the data presented are of superb quality, and the manuscript represents a tremendous leap in structural insight and imaging resolution for the field of malaria. I find the data is suitable for publication albeit minor adjustments are made (specially to Figure 1 and/or the description of the results shown in Figure 1, for consistency).
We agree that the value of this manuscript lies in the clarification of conflicting data, unprecedented structural insight, and providing a useful working model for the malaria parasite centrosome. Although this study is ultimately descriptive it forms the indispensable basis to generate more meaningful functional insight about centrosome biology and nuclear division. Some of the functional consequences worth considering are: i) The (at least) bipartite composition indicating that centrosome functionality is spatially spread throughout the nucleoplasm/cytoplasm boundary. ii) The delayed appearance of the centrin signal after tubulin signal allows the prediction that centrosome assembly is a staged process occurring over an elongated period of time. iii) The generally amorphous structure of the compartment predicts the involvement of yet to be uncovered matrix-like proteins harbouring microtubule nucleation sites. iv) Lastly, our model has important implications for the mechanism of centrosome duplication. In a centrosome containing centrioles (like in vertebrates), the duplication event can easily be explained by physical separation of the daughter and mother centrioles. Spindle pole body duplication in yeasts is achieved by de novo formation of a new one, which remains connected by a half bridge until it is split. The centriolar plaque organization revealed here suggests that we need an entirely new model of centrosome duplication (or splitting) to describe and understand this process in malaria parasites. We now address those points more explicitly in the discussion section (e.g. lines 375, 443, 467).
**Referee Cross-commenting**
I agree with all the other reviewer's comments. I'm glad the reviewers seem to be experts in the field of malaria cell division and have pointed out previous studies which were not appropriately referenced. I second those comments.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
**Summary:**
The manuscript by Simon et al have used advance cell biology technology like STED, expansion and live cell imaging to decipher the configuration of microtubules, centrin and nuclear pore during unconventional cell division process in malaria parasite. They have shown the dynamics of centrin and its localisation with respect to centriolar plaque that is characteristic of these parasite cell during schizogony> They also implicate from their studies that there is extended intranuclear compartment which is devoid of chromatin
**Major Comments**
Are the key conclusions convincing? Yes to some extent
Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?
*Some part are preliminary and speculative as there is no solid data supporting it. Please see below
- 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.
*Yes to substantiate their claim
- 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.
*They can do these quite quickly less than a month
- 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
The authors present beautiful imaging and some in depth structure using tomography and CLEM to show the location of centrin which is generally considered the marker for centrosome or Microtubule organising centre in malaria parasite. These approaches are still not been applied in Plasmodium and hence very informative. Though they present some advance microscopy but a lot of these concept for hemispindle were shown earlier in many light and super resolution microscopy studies. Authors claim that they are first to show that there is space between centrin and nucleus but it has been show previously in centrin studies in Plasmodium berghei using super resolution microscopy (Roques et al 2019 Fig1 and supplementary videos1&2) as well as expansion microscopy recently by group of Brochet etal 2021.
We thank the reviewer for the appreciation of our work. We are, indeed, not the first to describe the gap between centrin and tubulin or the nucleus. We just aimed to reiterate this finding, also visible in our data, in order to transition to the analysis of nuclear pore positioning to clarify whether centrin is actually extranuclear. Nevertheless, we should have cited the Roques and Bertiaux et al. studies again in this context, which we have now rectified (line 252).
In addition the microtubule dynamics was also recently shown with Kinesin5 live cell imaging for schizogony in Plasmodium berghei (PMID: 33154955) which author have omitted in their manuscript.
We thank the reviewer for pointing out the Kinesin-5 study by Zeeshan et al., which we failed to cite and discuss. We now state the findings of this publication and put it into the context of our work (see also answer to next point). Microtubule associated proteins, such as the microtubule plus end tracking EB1 and the aforementioned Kinesin-5, are indeed useful markers to investigate microtubule dynamics leading to the interesting results shown by Zeeshan et al. Nevertheless, we want to point out that labelling microtubule associated proteins (MAPs) remains an approximation of the underlying microtubule organization. As the authors in Zeeshan et al. indicate by themselves, Kinesin-5 does not decorate axonemal microtubules or the membrane-associated microtubule structure formed during cytokinesis in very late schizont stages. Further, colocalization between alpha-tubulin and kinesin-5 in schizont-stage parasites is not complete indicating a preferential decoration of certain sections of the microtubule structures (possibly the microtubule ends), which could only be resolved by super-resolution microscopy. Using a live cell dye, such as SPY555-tubulin, which directly binds to microtubules will provide a uniform labelling of any microtubule species and hopefully prove useful to the field in the future. Lastly, we present time-lapse microscopy analysis of blood stage cells, contrary to single time point images of live cells, providing a quantified chronology of microtubule reorganization at single cell level (with time stamps). Therefore, we feel that our claim, although it should be relativized, is formally speaking accurate.
It is also important that authors give valid discussion about previous studies on hemispindle, microtubule dynamics with respect to schizogony (PMID: 18693242; PMID: 11606229; PMID: 33154955) rather than giving the impression that they have given this concept first time on hemispindle dynamics and centrin location during schizogony.
We agree that those studies should be discussed in more detail. We are grateful to the reviewer for pointing out the Fowler et al. 2001 (PMID: 11606229) study. They use an antibody against gamma-tubulin to demonstrate its presence at the apical pole of subpellicular microtubules (f-MAST) in the merozoite and cytokinetic stages (line 102). However, we were unable to reveal a specific gamma-tubulin staining using the antibody used by them in the preceding schizont stage. After trying many different commercial gamma-tubulin antibodies and attempting to generate our own we now finally observe a gamma tubulin localization at the poles of intranuclear spindles in schizont stage, although the only successful antibody still displays some background staining, possibly including cross-reactivity with alpha or beta-tubulin (Fig. S4, line 237).
The highly insightful study by Mahajan et al. 2008 (PMID: 18693242) indeed suggests that centrin localizes away from the DNA and demonstrate the distinct localization from tubulin. They, however, likely due to the resolution limit of their microscopy techniques, speculate that the centrin signal is embedded in the membrane, while we could show by super-resolution and nuclear pore staining that centrin is distinct from the membrane (now Fig. 2A; line 257). The work done by Zeeshan et al. 2020 (PMID: 33154955) nicely shows dynamics of kinesin-5 in nuclear division. In schizont stages Kinesin-5 signal elongates and splits alongside the mitotic spindle with which it overlaps for the most part. Colocalization with centrin is less strong although the authors note some overlap. Our data suggest that centrin and tubulin are clearly distinct. In male gametes the authors show nicely time-resolved data of kinesin spreading along the elongating spindle, although hemispindles are not observed at this stage. We introduce and discuss these findings (lines 123, 432).
The concept of bipartite centrosome is already been discussed in Toxoplasma and the claim by authors in Plasmodium presented here is not substantiated experimentally. They showed that centrin is part of outer region while they do not show with any marker for the inner region. It will be very helpful if the authors use gamma tubulin or MORN1 to show the location with respect to centrin and microtubule. In the absence of this localisation the claims are preliminary and speculative. If the centrosomal protein complex is not involved in microtubule nucleation, then how the nucleation is happening. What are the molecules present in this amorphous matrix? It will be great to check the location of gamma-tubulin or some inner centrosome molecules described in Toxoplasma that is deemed to be MTOC.
We share the opinion that our Plasmodium data should be compared to Toxoplasma, while still being assessed independently. Despite Toxoplasma belonging to the apicomplexan the conclusion that their centrosomes should be organized in a similar fashion is by no means self-evident considering for example their significant evolutionary distance. Actually, several noteworthy morphological differences have already been well documented. i) Toxoplasma MTOC does contain centrioles in the outer core which is coherent with the centrin and gamma-tubulin localization in this region. ii) Toxoplasma MTOC contains an additional nuclear membrane protrusion enclosing the inner core. iii) mitotic microtubules in Toxoplasma are thought to penetrate the nuclear membrane to connect to centromeres. iv) the inner and the outer core are both extranuclear and therefore not to be equated with the intranuclear compartments. We now expand a bit on the discussion of the aforementioned differences (line 382). Nevertheless, we thank the reviewer for making us realize that the term “bipartite” is a poor choice to describe the centriolar plaque organization in this context. Therefore, we replaced it in the abstract (line 29) and the main text (line 375).
We acknowledge the fact that it would be desirable to show a marker localizing to the intranuclear compartment, and not only through visualizing the microtubule nucleation complex (Fig. 4A-B) and the positioning of the microtubule ends in this region (Fig. 3A). Concerning MORN1 we found no indication in the published localization data that it is, like in Toxoplasma, associated with the nucleus in Plasmodium species, where it is only found associated with the budding complex (and we are currently unable to procure an antibody) (line 422). We have attempted gamma-tubulin visualization on many occasions throughout the project (transgenic parasite lines, commercial antibodies, self-made antibodies) and only recently found an antibody revealing some specific signal. Indeed, we found localization at the poles of the spindles i.e. the intranuclear compartment (line 237). Unfortunately, this “best-possible staining” still showed some unspecific spindle staining likely resulting from cross-reactivity with alpha- or beta-tubulin causing us to put these data into the supplements (Fig. S4).
We had more luck with attempting a “new” type of staining, recently used in Plasmodium (Bertiaux & Balestra et al. 2021) using a fluorophore-coupled NHS-Ester in expanded samples. This chemical unspecifically stains proteins and revealed that the centrosomal region contains an exceptionally protein dense “hourglass-shaped” structure (Fig. 3F-H). Since the outer part of this structure colocalizes with centrin and the inner part overlaps with microtubules we assume that the centrosomal complex stretches throughout the nucleo-cytoplasmic boundary and fills part of the intranuclear compartment (line 320). Especially the highly protein dense region at the neck of the “hourglass” seems very coherent with the nuclear membrane embedded electron dense region which can be seen in electron microscopy (e.g. Fig. 3E & 4B). We feel that this staining strongly supports the presence of this novel intranuclear compartment.
The expansion microscopy is very nice and some of it presented in supplementary can be moved to main section.
Thanks for sharing our enthusiasm about this imaging technique. We have now selected a representative image of a hemispindle and mitotic spindle stage nucleus imaged by U-ExM and added it to the main section (Fig. 2B, line 231).
The localisation CenH3 is bit puzzling as it has been shown that centromere/ kinetochore cluster and are present during early and mid schizogony. The various foci with respect to nuclei are not what has been seen previously. Please discuss the difference in these two findings.
The localization pattern can easily be explained by the increased resolution of STED nanoscopy used in this study. Previous studies (e.g. Hoeijmakers et al. 2012 and Zeeshan et al. 2020) used classical confocal microscopy. Under those imaging conditions the individual foci seen here can´t be resolved and would, in accordance with the other studies, appear as one cluster. We slightly modified the text for more clarity (line 247).
Reviewer #2 (Significance (Required)):
- Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.
* This is more technical advancement on the subject of centrin by using STED, tomography and CLEM.
- Place the work in the context of the existing literature (provide references, where appropriate).
* This work has relevance relation to cell division during schizogony in asexual stages in par with Toxoplasma or in Apicomplexa in general
- State what audience might be interested in and influenced by the reported findings.
Working with Apicomplexa, Protist, cell division and mitosis.
- 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.
Working on Cell division in Plasmodium.
**Referee Cross-commenting**
I agree with the reviewers and some of the experiment suggested and the minor details have to be addressed. There are some loose ends and these suggestions will enhance clarity of the data. It is a very nice study and some of the comments suggested by reviewers will improve the manuscript. __
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
**Summary:**
The centrosome is the primary microtubule-organizing center (MTOC) in eukaryotic cells that nucleate spindle microtubules necessary for chromosome segregation. In most eukaryotic cells, the canonical centrosome is composed of centrioles surrounded by an electron-dense proteinaceous matrix named the pericentriolar matrix (PCM) competent for microtubule nucleation mitotic spindle assembly. Following the breakdown of the nuclear envelope breakdowns, the mitotic spindle microtubules gain access to the kinetochores of the condensed mitotic chromosomes. Once the mitotic spindle is fully developed, centrosomes are at opposite poles of the cells, and chromosomes are pulled toward opposite poles. Cell division completes with cytokinesis resulting in the active formation of two nuclei within two daughter cells. Interestingly, during its asexual replication cycle, the malaria parasite Plasmodium falciparum undergoes multiple asynchronous rounds of mitosis with segregation of uncondensed chromosomes followed by nuclear division within an intact nuclear envelope. The multi-nucleated cell is then subjected to a single round of cytokinesis that produces dozen of daughter cells. We know about the Plasmodium centrosome is that it is made of an acentriolar structure embedded in the nuclear envelope and serves as MTOC during cell division. However, the biogenesis and regulation of the Plasmodium centrosome are poorly understood. Given the peculiarity of the cell division in Plasmodium parasites, understanding the molecular mechanisms that drive and regulate MTOC duplication and maturation could unveil novel targets for the treatment of malaria. In this study, Simon et al. successfully applied challenging and cutting-edge microscopy techniques to monitor the dynamic formation of the spindle microtubules and MTOC during Plasmodium intraerythrocytic mitosis. In addition, they remarkably combined stimulated emission depletion (STED) with ultrastructure expansion microscopy to define an uncharacterized intranuclear compartment devoid of chromatin as the nucleation site of nuclear microtubules. And lastly, the authors adapted an in-resin correlative light and electron microscopy (CLEM) approach to define the centriolar plaque position in a novel intranuclear compartment with centrosomal function.
**Major comments:**
In the methods section, it is stated that across this study, three different anti-tubulin antibodies (alpha-tubulin B-5-1-2, alpha-tubulin TAT1, beta-tubulin KMX1) were used, and two anti-centrin antibodies (TgCentrin1 and PfCentrin3) were used, one of which seems to have been generated in this study (anti-PfCentrin3). It is unclear in the figures or results section when each of these antibodies was used, and the authors should give a rationale for using multiple antibodies in combination.
To label microtubules we used the mouse anti-alpha-tubulin B-5-1-2 (Sigma, T5168) antibody throughout the study. Except for U-ExM were we added two additional primary antibodies against tubulin. Due to the expansion of the samples the antibody binding epitopes are stretched out in space. This causes a significant reduction of local epitope concentration (expansion factor 4.5 in all directions results in ~ 80-fold increase in the volume), which can reduce the signal intensity. Adding multiple antibodies binding different epitopes of tubulin can compensate for this dilution effect to some degree, as has been shown before by Gao et al. 2018. At the same time the expansion contributes to the accessibility of the usually densely packed tubulin epitopes within the microtubule polymer, which certainly adds to the success of U-ExM. What the respective contributions of those effects are is not clear, but we found superior signal-to-noise ratios when combining three tubulin antibodies instead of using one. The TgCentrin1 antibody was only used in Fig. 2C (now Fig. 3B) and validated the localization pattern of our new PfCentrin3 antibody we used in the other pictures. We now provide clearer description of antibody usage in the methods section and a new supplemental table.
The anti-PfCentrin3 antibody seems to have been generated for this study. If this is the case, the authors should provide evidence that this antibody binds to the recombinant PfCentrin3 it was raised against and binds PfCentrin3 in parasite lysates.
The anti-PfCentrin3 antibody was, indeed, produced for this study and we should have provided our western blot data right away. We now show the requested blot, which shows bands at the appropriate size in parasite lysate as well as for the recombinant protein, in the supplements (Fig. S2, line 178).
In the first paragraph of the Results section, the authors' remark of centrin foci that they are "...only detectable later (Mov. S2) or sometimes not at all." In Figure 1 A-C, it is implied that the first observed division is the first nuclear division of that parasite. Given that some nuclei do not have a visible centrin focus, it cannot be concluded with certainty that these parasites only contain a single nucleus and that this is their first division. The authors would need to include a quantifiable DNA stain to show this unequivocally to show a single nucleus. It has undergone DNA replication, similar to Klaus et al., 2021 BioRxiv paper. In the absence of a DNA stain, the authors should reword to clarify that this is the first observed division and speculate that it is the first division of that nucleus, but the authors should draw no firm conclusions about the first division.
Indeed the variability in protein levels that can result from exogenous expression can lead to some cells not showing clear Centrin1-GFP foci. Although this is a rare event we wanted to acknowledge this observation. The live cell microtubule staining using Spy555-Tubulin we use is, however, highly specific and sensitive and would stain any nucleus undergoing division including the first one. If there would be more than one nucleus in the observed cell it would unequivocally show two clearly separated tubulin signals (hemispindle or mitotic spindle). To illustrate this we added Fig. 1B (line 148) showing two live parasites stained with SPY555-Tubulin plus a Hoechst-based dye showing one or two nuclei alongside the corresponding tubulin signal. We modified the text to clarify how we stage the parasite for time-lapse acquisition (line 154). We already extensively experimented with state of the art fluorogenic live cell DNA dyes (e.g. from Spirochrome and the Johnsson group) to visualize the nuclei directly in time lapse microscopy, but even at minimal concentrations they all significantly inhibit mitotic progression. We also add this information in the main text (line 150).
In the first paragraph of the Results section, the authors write: " We quantified the duration of hemispindle, accumulation and anaphase stages ...." Anaphase spindle fibers means that the sister chromatids are separated. In the absence of a centromeric marker like NDC80, it doesn't seem easy to claim the anaphase stage. The authors should write " extended spindle." The authors might also consider using the term collapsed spindle instead of accumulation to reflect the dynamic of the intranuclear microtubules during the blood-stage replication. The same modification should be made for Figure 1B, so we read " hemispindle, collapsed spindle and extended spindle."
We thank the reviewer for this suggestion, which is very much in line with a comment by Reviewer 1 on the definition of anaphase. We acknowledge that the term is ill-defined here. Further, it suggest a mitotic morphology analogous to the one observed in “classical” models (prophase, metaphase, anaphase,…), which is not fully appropriate. Consequently, we decided to adapt the suggested terminology in Fig. 1 (and also new Fig. 2) and in the text (line 160).
Based on the evidence in this study, it cannot be stated unequivocally that the centrosome is entirely extranuclear, at least not as it is implied in Figure 3C. In Supplementary Figure 4, the microtubules appear to be extruding from a circular structure that may either be intranuclear or span the nuclear envelope. In Supplementary Figure 6, the structure pointed to as the centrosome appears to be embedded within the nuclear membrane with a top structure on the cytosolic side of the nuclear envelope. Thus, the best support for an extranuclear centrosome comes from the CLEM images. Still, it is noteworthy that the double membrane of the nuclear envelope is not visible on this slice in the region where the centrin fluorescence is found. Considering some of the fluorescence pixels for centrin are outside the parasite plasma membrane, and some of the Hoechst pixels are outside the nuclear envelope, this data does not show unequivocally that centrosomes are entirely extranuclear. However, this argument would be strengthened if the authors performed a proteinase K protection assay (or something similar) to determine if Centrin1 and Centrin3 are exposed to the cytosol. However, in the absence of that or further evidence, the authors should dampen their claims about the centrosome being exclusively extranuclear, as represented in the schematic in figure 3C.
We thank the reviewer for this comment, which highlights an issue in our communication of our working model of the centriolar plaque. At no point we intended to claim that the centrosome is exclusively extranuclear. Rather, centrins, which are currently the only reliable marker proteins, localize to a subcompartment of the extranuclear region of the centriolar plaque. Additionally, the centrosome clearly contains an intranuclear region. The composition of this intranuclear compartment is elusive, except that it harbors microtubule nucleation sites. Indeed, our model in Fig. 3C (now Fig. 4C) is misleading and not well annotated. The newly added NHS-Ester staining fortifies this claim (Fig. 3F-H. Consequently, we corrected our working model by adding an explicit figure labelling (now Fig. 4C).
We apologize for the misleading labelling in Fig. S6 (now Fig. S7). The green arrow was intended to point out the electron dense region associated with the nuclear membrane, which has been seen in previous studies, and was not intended to represent the entire extended centriolar plaque. If anything, this smaller region might provide the link between the intra and extranuclear compartments that the reviewer also identified in Suppl. Fig. 4 (now Fig. 2D). We modified the annotation of the Fig. S7 and Fig. 4A-B accordingly, labelling it the “electron dense region”. More importantly, we hope that our newly added data using NHS-Ester staining of protein dense regions (Fig. 3F-H) highlights the spread of the centrosome across the nucleo-/cytoplasmic boundary more clearly.
Considering whether centrin is actually extranuclear, we feel that the data shown in Fig. 2A (now 3A) is convincing. We have, however, added two panels of the relevant regions showing centrin localization respective to the nuclear pore and adjusted the contrast as we acknowledge the limited “visibility” within the unadjusted panels. The fact, that the centrin signal slightly overlaps with the nuclear envelope in CLEM images can be explained by the relatively poor resolution of the widefield microscope we had to use to image the sections. From the other super-resolution images in the manuscript, we know that the perimeter of the better resolved centrin signal is significantly smaller. Otherwise one had to assume from the CLEM data that centrin is also in the cytosol of the red blood cell and that DNA is localized outside the nucleus. On a similar note the fluorescence image is, contrary to the tomography image, a single slice since the thickness of the sample section (about 200nm) is significantly below the z-resolution (about 500nm) of a fluorescence microscope.
Throughout the study, the level of biological replication is unclear. The authors rigorously include all the data points for each of their graphs and the total number of images/videos quantified. And what needs to be added, in either the figure legends or a methods section, is the number of biological replicates for each of these measures came from.
We have added the number of replicas in the figure legends.
**Minor comments:**
STED is present as an acronym in the abstract and should be spelled out in full and clarified that it is a super-resolution microscopy technique.
We opted to remove STED from the abstract (leaving it at super-resolution, which includes expansion microscopy) to avoid disrupting the “flow” of the abstract and now spell out the acronym at the first mention in the introduction (line 127).
The second paragraph of the Results section states that ring and early trophozoite stage parasites do not express tubulin or centrin. Still, only an early trophozoite is shown in Supplementary Figure 2. Therefore, the authors should either include a similar image of a ring-stage parasite or remove ring-stage parasites from that statement.
We have removed the ring stages from the statement.
The second paragraph of the Results section contains the sentence, "At which point tubulin is reorganized into the bipolar microtubule array, which then forms the mitotic spindle cannot be resolved here." The authors are implying that the point at which tubulin is reorganized into the microtubule array, which goes on to form the mitotic spindle, cannot be resolved here. This is not particularly clear, though, and this sentence could be reworded for clarity.
We reformulated the sentence to clarify the point we failed to make with the previous wording (line 188).
The second paragraph of the Results section contains some statements about the results without referencing the figures that these statements come from. The authors should clarify this to make clear which figures each statement refers to.
We added more references to the appropriate figure throughout the paragraph (lines 188, 219, 223).
In the third paragraph of the introduction section, the authors write, " Centriolar plaques seem partially embedded in the nuclear membrane, but their positioning relative to the nuclear pore-like "fenestra" remains unclear." Unfortunately, the lack of reference did not allow me to understand if the authors state literature or comment on past published results.
We added the reference which was incorrectly positioned before the sentence instead of at the end (line 82).
the authors could add some references:
Second section of the introduction: " the 8-28 nuclei are packaged into individual daughter cells, called merozoites ( Rudlaff et al. 2019 PMID: 31097714)
Third section of the introduction: " The centrosome of P.falciparum is called centriolar plaque" ( Arnot et al. 2011, Sinden 1991a); " the nuclear pore-like "fenestra" remains unclear (Wall et al. 2018; Zeeshan et al. 2020).
Fourth section of the introduction: " tubulin antibody staining are extensive structures measuring around 2-4um ( Ref?)
When the authors introduce subpellicular microtubules of segmented schizonts, a reference to a study that shows these structures should be included.
A previous study that shows the distinct structure of microtubule minus ends should be cited when this structure is described.
Third section of the results, the authors should cite Bertiaux et al. 2021 with the Gambarotto et al. 2019 paper regarding U-ExM.
We apologize for missing some important references or putting them in the wrong position. We now added all the references or cite them again at the appropriate locations throughout the text.
Figure 1E shows hemispindle and mitotic spindle lengths of U-ExM expanded parasites, but the position within the figure and figure legend implies that these lengths were determined unexpanded parasites. Therefore, it should be stated in the figure legend that these measurements come from U-ExM expanded parasites. Moreover, I encourage the authors to include U-ExM images in the main figures. The images are beautiful, represent a significant technical achievement, and directly relate to Figure 1E. To the best of my knowledge, this is only the second study to perform expansion microscopy on Plasmodium and the first to use PFA-fixed parasites and a nuclear stain. It would be valuable for the Plasmodium and ExM communities to see this technical advancement represented in the main text.
We thank the reviewer for the appreciation of our ExM data and added it to Fig. 2B before the quantification of the microtubule length and number and added the information to the legend.
In the second paragraph of the Results section, the authors write, " but clearly display the microtubule cytoskeleton associated with the inner membrane complex." It would bring clarity to define in few words what the IMC is.
We included a short definition of the IMC (line 223).
The methods section details that the length of microtubules was determined by dividing the observed values by an expansion factor of 4.5. If the authors recorded the expansion factors of their gels, this data should be included, and how it was recorded should be stated in the methods. If not, the authors should include the rationale of using an expansion factor of 4.5 as this is slightly different from the previously published expansion factor of P. falciparum of 4.3.
We recorded the expansion factor by measuring the gel size pre and post expansion with a ruler and found a factor of 4.5 on average. We added this information in the methods (line 688).
There are several parasite lines used in this study, and some figures are not clear what parasite line was used. Could the authors please include the parasite lines in the figure legends of Figure 1 D-F, Figure 3, Supplementary Figures 1-2, and Supplementary Figures 4-7?
We added the parasite line information in the legends as requested.
Nuclear pore complexes, of which Nup313 is a component, can have cytoplasmic, integral, and nuclear-facing components. If it has been shown previously that PfNup313 is the homolog of Nup214 in vertebrates present on the cytosolic side of NPC, this should be stated. If not, then it should be clarified that it is unknown whether Nup313 faces the cytoplasm, nucleus, or is embedded in the NE, as this has implications for the colocalization of Nup313 and Centrin.
Nuclear pore proteins are very poorly conserved in P. falciparum and Nup313 has only been recently identified as such (Kehrer et al. 2018) mainly by the presence of FG-repeats (as for all the other newly defined proteins). The only related ortholog that can be found through BLAST search against humans, yeasts, and Arabidopsis is Nup100 from S. cerevisiae. ScNup100 is a central pore localizing protein but the sequence similarity to Nup313 is low. We are not aware of any findings showing relatedness to vertebrate Nup214, while sequence analysis rather indicates the absence of orthology. To clearly demonstrate the individual positioning of the few known Nups within the parasite´s nuclear pore complex would require a dedicated long-term project. However, due to the presence of FG-repeats one can assume that it is part of the central FG-Nups layer rather than of the intranuclear basket or the cytoplasmic filaments (line 255). Therefore it would localize more closely to the nuclear envelope than the latter. Either way, a clear gap between centrin and Nup313 signal can be identified and colocalization has not been observed. These data indicate that the exact position of Nup313 on the cytoplasmic, integral or nuclear-facing site is not decisive for the conclusions made in this study and our observations preclude scenarios where centrin is not extranuclear.
It seems from the image in Figure 2C that DRAQ5 and Hoechst have at least visually indistinguishable localizations. Have the authors taken any STED deconvolved images of nuclei stained with both Hoechst and DRAQ5? Considering the striking increase in detail of the Hoechst signal in STED deconvolved images, it may be informative both to this study and to people who work on chromatin organization what the chromatin staining looks like in the absence of bias towards chromatin state.
It would, indeed, be interesting to analyse chromatin organization by those means, but DRAQ5 is not a STED compatible dye, highly prone to bleaching, and therefore not suitable for such analysis. Being an infrared dye DRAQ5 is compared to the UV excited Hoechst also yielding a reduced spatial resolution, which is limited by the emitted wave length.
For the tomography and TEM images, the centrosome is indicated with an arrow, but it isn't entirely clear what that arrow is pointing to for some images. It would be clearer if the centrosome were outlined in green, like the NE, rather than just an arrow. This is particularly important for Supplementary Figure 4, where to my eye, it appears that the microtubules inside the chromatin-free region are coming directly out of a circular structure, which could be interpreted as the centriolar plaque.
The reviewer is right to point out the use of arrows for centrosome annotation. It was intended for orientation of readers to indicate the “likely position of the centriolar plaque” since a clear boundary around the centrosome can´t be defined. It would have been more precise to indicate that the arrow is pointing at the electron dense region associated with the nuclear membrane, which is of course only one of the sub-regions of the centrosome. This is particularly important since we want to emphasize the extended dimensions of the centrosome. Consequently, we modified the annotation to “electron dense region” in all concerned figures and corresponding legends.
The ordering of Figure 2A-C seems to imply that the DNA-free region was measured in the STED deconvolved images, but the methods imply that it was in the confocal images. The authors should clarify this in the figure legend or by rearranging B and C's order.
Hoechst signal was indeed acquired and measured in confocal mode and to avoid confusion we have changed the order of the figures (now Fig. 3B-C) as suggested.
The authors should provide some more detail on how the DNA-free zone was measured. For example, was it measured on single slices or maximum intensity projections? Was it measured from the middle, far, or near side of the centrin focus? Etc.
The measurement was carried out in the slice where the DNA-free zone was in focus. Depth was measured from below the centrin signal until the “bottom” of the DNA-free zone. We hoped that the little schematic above the figure would clarify this question, but acknowledge the need to more clearly explain the measurement method, which we now do in the corresponding figure legend (Fig. 3C).
The methods state that the mCherry signal in figure 2C was detected using a mCherry nanobody. This should be clarified in the figure legends as it currently seems as if we see endogenous mCherry fluorescence.
The visible signal is certainly a combination of the mCherry plus the “boosting” effect from the Atto594-coupled nanobody that we added. Clearly, this should be mentioned in the figure legend, which we now do.
The data in Supplementary Figure 4 seems vital to the interpretation of the study. Therefore, for clarity, I encourage the authors to include Supplementary Figure 4 in Figure 2.
We share the reviewers view on these data and moved them to the main figures (now Fig. 3D).
In the last sentence of the discussion, it is unclear what the authors mean by how the nuclear compartment "splits," could they please clarify?
We were referring to the event of centrosome duplication, which has to occur during nuclear division. In a structure without centrioles or a spindle pole body structure forming a half bridge we therefore need a new model to explain how the two poles of the spindle are formed. Potential modes are splitting or de novo assembly. This aspect, as also pointed out by other reviewer, warrants a bit more explanation, which can now be found in the discussion (line 468).
If the pArl-PfCentrin3-GFP plasmid or pDC2-cam-coCas9-U6.2-hDHFR have been published previously, the respective studies should be cited. If not, the study where the vector backbones were first established should be cited.
We have now cited the original studies publishing the vector backbones for the first time in the methods (lines 490, 501).
From the current text, it is not clear that the Nup313 tagged parasites also had a GlmS ribozyme. It is shown in Supplementary Figure 3, but the authors should clarify either in the text of the results, or figure legends, that this parasite line was Nup313_3xHA_GlmS
The Nup313-tagged line indeed has a glms ribozyme after the HA-tag, which we now mention in the figure legends.
In the plasmid constructs section of the methods, the authors list several primers by number but not by sequence. Instead, the authors should include the sequence and orientation of each of the primers mentioned in a table as supplementary data.
This is a good suggestion. We have generated a table at the end of the supplementary data file and on this occasion we also added tables of all the antibodies and dyes used in this study.
The authors should cite the study where the TgCentrin1 antibody was generated and provide the Rat anti-HA 3F10 antibody catalog number, as catalog numbers are provided for other commercial primary antibodies.
We now provide the missing catalog numbers in the supplemental data table.
There is an issue with the formatting of the journal-title in the Kukulski et al. reference.
Thank you for noticing this error, which we now corrected.
Reviewer #3 (Significance (Required)):
The genome of P. falciparum is fully sequenced; however, over 50% of encoded proteins are of unknown function, with many of these proteins unique to Plasmodium parasites. By identifying and characterizing essential biological processes, especially those divergent from human host cell processes, we will formulate ways to interfere with them by developing novel antimalarial drugs. The process of Plasmodium cell division differs from the classical cell cycle of its human host. In the study led by Caroline Simon, authors successfully utilized recent developments of super-resolution microscopies on expanded parasites to identify novel features of cell division machinery of the malaria blood-stage parasite.
Simon et al.'s work highlight the growing interest in the diversity of cell division mode of Apicomplexan parasites, which will likely contribute to a deeper understanding of the origin and functional role of the centrosome in eukaryotic life. In 2020, the Open Biology journal published a unique article collection named Focus on Centrosome Biology showcasing research that advanced our knowledge on centrosome function, evolution and abnormalities. In addition, the reported findings will interest research groups studying cell cycle regulation and evolution beyond the field of parasitology.
Our lab studies the peculiar cell cycle of Plasmodium falciparum to gain a functional understanding of mechanistic principles of nuclear envelope assembly and integrity during the cell division of the human malaria parasite.
**Referee Cross-commenting**
It is a wonderful study, and once all reviewer's comments are addressed, the manuscript should be in excellent shape for publication.
-
Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.
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Referee #3
Evidence, reproducibility and clarity
Summary:
The centrosome is the primary microtubule-organizing center (MTOC) in eukaryotic cells that nucleate spindle microtubules necessary for chromosome segregation. In most eukaryotic cells, the canonical centrosome is composed of centrioles surrounded by an electron-dense proteinaceous matrix named the pericentriolar matrix (PCM) competent for microtubule nucleation mitotic spindle assembly. Following the breakdown of the nuclear envelope breakdowns, the mitotic spindle microtubules gain access to the kinetochores of the condensed mitotic chromosomes. Once the mitotic spindle is fully developed, centrosomes are at opposite poles of the cells, and chromosomes are pulled toward opposite poles. Cell division completes with cytokinesis resulting in the active formation of two nuclei within two daughter cells. Interestingly, during its asexual replication cycle, the malaria parasite Plasmodium falciparum undergoes multiple asynchronous rounds of mitosis with segregation of uncondensed chromosomes followed by nuclear division within an intact nuclear envelope. The multi-nucleated cell is then subjected to a single round of cytokinesis that produces dozen of daughter cells. We know about the Plasmodium centrosome is that it is made of an acentriolar structure embedded in the nuclear envelope and serves as MTOC during cell division. However, the biogenesis and regulation of the Plasmodium centrosome are poorly understood. Given the peculiarity of the cell division in Plasmodium parasites, understanding the molecular mechanisms that drive and regulate MTOC duplication and maturation could unveil novel targets for the treatment of malaria. In this study, Simon et al. successfully applied challenging and cutting-edge microscopy techniques to monitor the dynamic formation of the spindle microtubules and MTOC during Plasmodium intraerythrocytic mitosis. In addition, they remarkably combined stimulated emission depletion (STED) with ultrastructure expansion microscopy to define an uncharacterized intranuclear compartment devoid of chromatin as the nucleation site of nuclear microtubules. And lastly, the authors adapted an in-resin correlative light and electron microscopy (CLEM) approach to define the centriolar plaque position in a novel intranuclear compartment with centrosomal function.
Major comments:
- In the methods section, it is stated that across this study, three different anti-tubulin antibodies (alpha-tubulin B-5-1-2, alpha-tubulin TAT1, beta-tubulin KMX1) were used, and two anti-centrin antibodies (TgCentrin1 and PfCentrin3) were used, one of which seems to have been generated in this study (anti-PfCentrin3). It is unclear in the figures or results section when each of these antibodies was used, and the authors should give a rationale for using multiple antibodies in combination.
- The anti-PfCentrin3 antibody seems to have been generated for this study. If this is the case, the authors should provide evidence that this antibody binds to the recombinant PfCentrin3 it was raised against and binds PfCentrin3 in parasite lysates.
- In the first paragraph of the Results section, the authors' remark of centrin foci that they are "...only detectable later (Mov. S2) or sometimes not at all." In Figure 1 A-C, it is implied that the first observed division is the first nuclear division of that parasite. Given that some nuclei do not have a visible centrin focus, it cannot be concluded with certainty that these parasites only contain a single nucleus and that this is their first division. The authors would need to include a quantifiable DNA stain to show this unequivocally to show a single nucleus. It has undergone DNA replication, similar to Klaus et al., 2021 BioRxiv paper. In the absence of a DNA stain, the authors should reword to clarify that this is the first observed division and speculate that it is the first division of that nucleus, but the authors should draw no firm conclusions about the first division.
- In the first paragraph of the Results section, the authors write: " We quantified the duration of hemispindle, accumulation and anaphase stages ...." Anaphase spindle fibers means that the sister chromatids are separated. In the absence of a centromeric marker like NDC80, it doesn't seem easy to claim the anaphase stage. The authors should write " extended spindle." The authors might also consider using the term collapsed spindle instead of accumulation to reflect the dynamic of the intranuclear microtubules during the blood-stage replication. The same modification should be made for Figure 1B, so we read " hemispindle, collapsed spindle and extended spindle."
- Based on the evidence in this study, it cannot be stated unequivocally that the centrosome is entirely extranuclear, at least not as it is implied in Figure 3C. In Supplementary Figure 4, the microtubules appear to be extruding from a circular structure that may either be intranuclear or span the nuclear envelope. In Supplementary Figure 6, the structure pointed to as the centrosome appears to be embedded within the nuclear membrane with a top structure on the cytosolic side of the nuclear envelope. Thus, the best support for an extranuclear centrosome comes from the CLEM images. Still, it is noteworthy that the double membrane of the nuclear envelope is not visible on this slice in the region where the centrin fluorescence is found. Considering some of the fluorescence pixels for centrin are outside the parasite plasma membrane, and some of the Hoechst pixels are outside the nuclear envelope, this data does not show unequivocally that centrosomes are entirely extranuclear. However, this argument would be strengthened if the authors performed a proteinase K protection assay (or something similar) to determine if Centrin1 and Centrin3 are exposed to the cytosol. However, in the absence of that or further evidence, the authors should dampen their claims about the centrosome being exclusively extranuclear, as represented in the schematic in figure 3C.
- Throughout the study, the level of biological replication is unclear. The authors rigorously include all the data points for each of their graphs and the total number of images/videos quantified. And what needs to be added, in either the figure legends or a methods section, is the number of biological replicates for each of these measures came from.
Minor comments:
- STED is present as an acronym in the abstract and should be spelled out in full and clarified that it is a super-resolution microscopy technique.
- The second paragraph of the Results section states that ring and early trophozoite stage parasites do not express tubulin or centrin. Still, only an early trophozoite is shown in Supplementary Figure 2. Therefore, the authors should either include a similar image of a ring-stage parasite or remove ring-stage parasites from that statement.
- The second paragraph of the Results section contains the sentence, "At which point tubulin is reorganized into the bipolar microtubule array, which then forms the mitotic spindle cannot be resolved here." The authors are implying that the point at which tubulin is reorganized into the microtubule array, which goes on to form the mitotic spindle, cannot be resolved here. This is not particularly clear, though, and this sentence could be reworded for clarity.
- The second paragraph of the Results section contains some statements about the results without referencing the figures that these statements come from. The authors should clarify this to make clear which figures each statement refers to.
- In the third paragraph of the introduction section, the authors write, " Centriolar plaques seem partially embedded in the nuclear membrane, but their positioning relative to the nuclear pore-like "fenestra" remains unclear." Unfortunately, the lack of reference did not allow me to understand if the authors state literature or comment on past published results.
- the authors could add some references: • Second section of the introduction: " the 8-28 nuclei are packaged into individual daughter cells, called merozoites ( Rudlaff et al. 2019 PMID: 31097714) • Third section of the introduction: " The centrosome of P.falciparum is called centriolar plaque" ( Arnot et al. 2011, Sinden 1991a); " the nuclear pore-like "fenestra" remains unclear (Wall et al. 2018; Zeeshan et al. 2020). • Fourth section of the introduction: " tubulin antibody staining are extensive structures measuring around 2-4um ( Ref?) • When the authors introduce subpellicular microtubules of segmented schizonts, a reference to a study that shows these structures should be included. • A previous study that shows the distinct structure of microtubule minus ends should be cited when this structure is described. • Third section of the results, the authors should cite Bertiaux et al. 2021 with the Gambarotto et al. 2019 paper regarding U-ExM.
- Figure 1E shows hemispindle and mitotic spindle lengths of U-ExM expanded parasites, but the position within the figure and figure legend implies that these lengths were determined unexpanded parasites. Therefore, it should be stated in the figure legend that these measurements come from U-ExM expanded parasites. Moreover, I encourage the authors to include U-ExM images in the main figures. The images are beautiful, represent a significant technical achievement, and directly relate to Figure 1E. To the best of my knowledge, this is only the second study to perform expansion microscopy on Plasmodium and the first to use PFA-fixed parasites and a nuclear stain. It would be valuable for the Plasmodium and ExM communities to see this technical advancement represented in the main text.
- In the second paragraph of the Results section, the authors write, " but clearly display the microtubule cytoskeleton associated with the inner membrane complex." It would bring clarity to define in few words what the IMC is.
- The methods section details that the length of microtubules was determined by dividing the observed values by an expansion factor of 4.5. If the authors recorded the expansion factors of their gels, this data should be included, and how it was recorded should be stated in the methods. If not, the authors should include the rationale of using an expansion factor of 4.5 as this is slightly different from the previously published expansion factor of P. falciparum of 4.3.
- There are several parasite lines used in this study, and some figures are not clear what parasite line was used. Could the authors please include the parasite lines in the figure legends of Figure 1 D-F, Figure 3, Supplementary Figures 1-2, and Supplementary Figures 4-7?
- Nuclear pore complexes, of which Nup313 is a component, can have cytoplasmic, integral, and nuclear-facing components. If it has been shown previously that PfNup313 is the homolog of Nup214 in vertebrates present on the cytosolic side of NPC, this should be stated. If not, then it should be clarified that it is unknown whether Nup313 faces the cytoplasm, nucleus, or is embedded in the NE, as this has implications for the colocalization of Nup313 and Centrin.
- It seems from the image in Figure 2C that DRAQ5 and Hoechst have at least visually indistinguishable localizations. Have the authors taken any STED deconvolved images of nuclei stained with both Hoechst and DRAQ5? Considering the striking increase in detail of the Hoechst signal in STED deconvolved images, it may be informative both to this study and to people who work on chromatin organization what the chromatin staining looks like in the absence of bias towards chromatin state.
- For the tomography and TEM images, the centrosome is indicated with an arrow, but it isn't entirely clear what that arrow is pointing to for some images. It would be clearer if the centrosome were outlined in green, like the NE, rather than just an arrow. This is particularly important for Supplementary Figure 4, where to my eye, it appears that the microtubules inside the chromatin-free region are coming directly out of a circular structure, which could be interpreted as the centriolar plaque.
- The ordering of Figure 2A-C seems to imply that the DNA-free region was measured in the STED deconvolved images, but the methods imply that it was in the confocal images. The authors should clarify this in the figure legend or by rearranging B and C's order.
- The authors should provide some more detail on how the DNA-free zone was measured. For example, was it measured on single slices or maximum intensity projections? Was it measured from the middle, far, or near side of the centrin focus? Etc.
- The methods state that the mCherry signal in figure 2C was detected using a mCherry nanobody. This should be clarified in the figure legends as it currently seems as if we see endogenous mCherry fluorescence.
- The data in Supplementary Figure 4 seems vital to the interpretation of the study. Therefore, for clarity, I encourage the authors to include Supplementary Figure 4 in Figure 2.
- In the last sentence of the discussion, it is unclear what the authors mean by how the nuclear compartment "splits," could they please clarify?
- If the pArl-PfCentrin3-GFP plasmid or pDC2-cam-coCas9-U6.2-hDHFR have been published previously, the respective studies should be cited. If not, the study where the vector backbones were first established should be cited.
- From the current text, it is not clear that the Nup313 tagged parasites also had a GlmS ribozyme. It is shown in Supplementary Figure 3, but the authors should clarify either in the text of the results, or figure legends, that this parasite line was Nup313_3xHA_GlmS
- In the plasmid constructs section of the methods, the authors list several primers by number but not by sequence. Instead, the authors should include the sequence and orientation of each of the primers mentioned in a table as supplementary data.
- The authors should cite the study where the TgCentrin1 antibody was generated and provide the Rat anti-HA 3F10 antibody catalog number, as catalog numbers are provided for other commercial primary antibodies. There is an issue with the formatting of the journal-title in the Kukulski et al. reference.
Significance
The genome of P. falciparum is fully sequenced; however, over 50% of encoded proteins are of unknown function, with many of these proteins unique to Plasmodium parasites. By identifying and characterizing essential biological processes, especially those divergent from human host cell processes, we will formulate ways to interfere with them by developing novel antimalarial drugs. The process of Plasmodium cell division differs from the classical cell cycle of its human host. In the study led by Caroline Simon, authors successfully utilized recent developments of super-resolution microscopies on expanded parasites to identify novel features of cell division machinery of the malaria blood-stage parasite.
Simon et al.'s work highlight the growing interest in the diversity of cell division mode of Apicomplexan parasites, which will likely contribute to a deeper understanding of the origin and functional role of the centrosome in eukaryotic life. In 2020, the Open Biology journal published a unique article collection named Focus on Centrosome Biology showcasing research that advanced our knowledge on centrosome function, evolution and abnormalities. In addition, the reported findings will interest research groups studying cell cycle regulation and evolution beyond the field of parasitology.
Our lab studies the peculiar cell cycle of Plasmodium falciparum to gain a functional understanding of mechanistic principles of nuclear envelope assembly and integrity during the cell division of the human malaria parasite.
Referee Cross-commenting
It is a wonderful study, and once all reviewer's comments are addressed, the manuscript should be in excellent shape for publication.
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Referee #2
Evidence, reproducibility and clarity
Summary:
The manuscript by Simon et al have used advance cell biology technology like STED, expansion and live cell imaging to decipher the configuration of microtubules, centrin and nuclear pore during unconventional cell division process in malaria parasite. They have shown the dynamics of centrin and its localisation with respect to centriolar plaque that is characteristic of these parasite cell during schizogony> They also implicate from their studies that there is extended intranuclear compartment which is devoid of chromatin
Major Comments
- Are the key conclusions convincing? Yes to some extent
- Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? *Some part are preliminary and speculative as there is no solid data supporting it. Please see below
- 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. *Yes to substantiate their claim
- 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. *They can do these quite quickly less than a month.
- 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
The authors present beautiful imaging and some in depth structure using tomography and CLEM to show the location of centrin which is generally considered the marker for centrosome or Microtubule organising centre in malaria parasite. These approaches are still not been applied in Plasmodium and hence very informative. Though they present some advance microscopy but a lot of these concept for hemispindle were shown earlier in many light and super resolution microscopy studies. Authors claim that they are first to show that there is space between centrin and nucleus but it has been show previously in centrin studies in Plasmodium berghei using super resolution microscopy (Roques et al 2019 Fig1 and supplementary videos1&2) as well as expansion microscopy recently by group of Brochet etal 2021. In addition the microtubule dynamics was also recently shown with Kinesin5 live cell imaging for schizogony in Plasmodium berghei (PMID: 33154955) which author have omitted in their manuscript. It is also important that authors give valid discussion about previous studies on hemispindle, microtubule dynamics with respect to schizogony (PMID: 18693242; PMID: 11606229; PMID: 33154955) rather than giving the impression that they have given this concept first time on hemispindle dynamics and centrin location during schizogony. The concept of bipartite centrosome is already been discussed in Toxoplasma and the claim by authors in Plasmodium presented here is not substantiated experimentally. They showed that centrin is part of outer region while they do not show with any marker for the inner region. It will be very helpful if the authors use gamma tubulin or MORN1 to show the location with respect to centrin and microtubule. In the absence of this localisation the claims are preliminary and speculative. If the centrosomal protein complex is not involved in microtubule nucleation, then how the nucleation is happening. What are the molecules present in this amorphous matrix? It will be great to check the location of gamma-tubulin or some inner centrosome molecules described in Toxoplasma that is deemed to be MTOC.
Minor comments:
- Specific experimental issues that are easily addressable.
- Are prior studies referenced appropriately? Partially
- 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? To gamma tubulin and some reference, move expansion microscopy
Minor comments:
- Specific experimental issues that are easily addressable.
- Are prior studies referenced appropriately? Partially
- 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? To perform experiments with gamma tubulin and add some references, move expansion microscopy.
Minor comments:
- Specific experimental issues that are easily addressable.
- Are prior studies referenced appropriately? Partially
- 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? To gamma tubulin and some reference, move expansion microscopy
Minor comments:
- Specific experimental issues that are easily addressable.
- Are prior studies referenced appropriately? Partially
- 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? To gamma tubulin and some reference, move expansion microscopy
The expansion microscopy is very nice and some of it presented in supplementary can be moved to main section. The localisation CenH3 is bit puzzling as it has been shown that centromere/ kinetochore cluster and are present during early and mid schizogony. The various foci with respect to nuclei are not what has been seen previously. Please discuss the difference in these two findings.
Significance
- Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.
- This is more technical advancement on the subject of centrin by using STED, tomography and CLEM.
- Place the work in the context of the existing literature (provide references, where appropriate).
- This work has relevance relation to cell division during schizogony in asexual stages in par with Toxoplasma or in Apicomplexa in general
- State what audience might be interested in and influenced by the reported findings. Working with Apicomplexa, Protist, cell division and mitosis.
- 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.
Working on Cell division in Plasmodium.
Referee Cross-commenting
I agree with the reviewers and some of the experiment suggested and the minor details have to be addressed. There are some loose ends and these suggestions will enhance clarity of the data. It is a very nice study and some of the comments suggested by reviewers will improve the manuscript.
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Referee #1
Evidence, reproducibility and clarity
The manuscript by Simon and collaborators addresses the dynamic changes of spindle and hemi-spindle microtubules occurring along schizogony in Plasmodium falciparum. The work explores the temporal correlation of the changes observed in intranuclear spindles with changes at the level of the centriolar plaque; the nuclear microtubule organizing center of these parasites, using centrin as a bona fide marker of the structure. The study shows that spindle microtubules organize from an intranuclear region, devoid of chromatin, distinct from the centrin region which had not been observed or described before. It further shows that centrin does not localize at the nuclear envelope, but it is actually extranuclear.
This work significantly expands on previous knowledge regarding the functional and spatial organization of the nucleus in P. falciparum, and the structure once defined as "an electron dense mass on the nuclear envelope." It uses state of the art microscopy approaches such as STED, UExM and CLEM, in combination with immunolabeling, dyes and parasites over expressing fluorescent protein fusions, to address these questions.
Major comments:
- Are the key conclusions convincing? I find the manuscript successfully addresses the posed questions. The data presented supports the conclusions.
- Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?
- 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. No
- 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. N/A
- 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
Minor comments:
- Specific experimental issues that are easily addressable.
On the data shown in Figure 1, it is unclear to me what elements are taken into account to define "anaphase." Anaphase could be defined by using chromatin markers - such as CenH3- which have been identified in Plasmodium and the authors make use of in Figure 1F.
- Are prior studies referenced appropriately?
The authors state that "with the exception of centrins and gamma tubulins" few canonical centrosome components are conserved in Plasmodium. These parasites are in fact able to assemble a more or less canonical centriole for microgamete basal body formation. Widely conserved centriolar components such as Sas6 are coded by the malaria genome, and have been characterized previously. This work is neither referenced nor discussed in the manuscript.
- Are the text and figures clear and accurate?
I find the timings shown in Figure 1A, with respect to the schematic quantification shown in Figure 1B, confusing. Shown as it is, one naturally correlates the images on Fig1A above with the cell cycle progression timing shown on Fig1B, below. However, by time 260min, for example, two somewhat adjacent centrin signals can be observed. Though this is defined as anaphase- by an unspecified criterium- this could very well be representative of metaphase. Nonetheless, the timing shown on Figure 1B for "anaphase" onset is 170min, which is inconsistent with the images above. I suggest that either, the quantification is shown in a different format (ex. bar plots) which could then better reflect the cell to cell variations observed (by use of error bars, for example)or that the figure explanation in the results section clarifies this issue. As presented, the data in Figure 1C is rather uninformative. A pattern could be more immediately extracted if dots corresponding to subsequent appearance of centrin dots in the same nucleus were connected to each other.
- Do you have suggestions that would help the authors improve the presentation of their data and conclusions?
There are a number of edits required on the text. Row numbers would have been helpful in pointing these out. I point some edits below, but thorough revision of the manuscript for grammatical and synthetic errors would be beneficial. • Cytokinetic segmeter - please replace with "segmented" • Please refer to Figure 1D when appropriate - there is quite an extensive paragraph describing the results shown on this figure, but it is only referenced at the start. • "..., as did the and the number of branches per nucleus,..." please rewrite as appropriate.
Significance
This manuscript could be interested to a wide audience interested in cell cycle, cell division, cell organization and organelle positioning, infectious diseases and microscopy. However, the introduction assumes that readers are somewhat experts in the malaria field. I suggest the authors include a brief introduction of the malaria life cycle, and a schematic representation of the division mode. This will help non-experts follow the narrative more easily.
This work rectifies long-standing inconsistencies observed by different experimental approaches in the nuclear organization of malaria parasites during schizogony. However, what the functional consequences of the alternative modes of spindle organization in malaria could be, are not clearly stated or discussed. In this respect, as it stands, the manuscript is rather descriptive and lacks mechanistic insight. Nonetheless, the data presented are of superb quality, and the manuscript represents a tremendous leap in structural insight and imaging resolution for the field of malaria. I find the data is suitable for publication albeit minor adjustments are made (specially to Figure 1 and/or the description of the results shown in Figure 1, for consistency).
Referee Cross-commenting
I agree with all the other reviewer's comments. I'm glad the reviewers seem to be experts in the field of malaria cell division and have pointed out previous studies which were not appropriately referenced. I second those comments.
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Reply to the reviewers
Reviewer 1
This paper proposes a noise-aware approach SCRaPL for modelling the associations of single cell multi-omic data. For gene expression, it uses Poisson-lognormal model. For DNAm data, it uses Binomial noise model which explicitly takes into account the average within the region. The Bayesian hierarchical framework employed by SCRaPL could achieve higher sensitivity and better robustness in identifying correlations, and also offer a template for the application of more complex analysis techniques to multi-omics data. The symbols of this paper are a little bit confusing, and I suggest authors to carefully check them.
We thank the reviewer for his/ her appreciation, and apologise for the confusion arising from the dense notation, which we will thoroughly revise.
- The symbols used in this paper are messy. For example, "1" and "2" are subscripts in Eq.(2) but become superscripts in Figure 5. Besides, there are many symbols not explained such as mj, Hj, Ψ0, etc. Also, I don't know if x{j,i}^{(1)} , x{j,i}^{(2)} in Figure 5 are same with x{ij1} and x{ij2} in Eq.(3). There are many places mismatch, authors should check carefully.
- Why the equations in Fig.5 are totally different with Section 4.2? For example, pj ∼Beta(αj ,βj ) in Fig.5 but ρj ∼ Beta−1,1 in Eq.(8).
We apologise for the notational confusion, this will be fully revised.
The paper involves a lot of hyper-parameters which doesn't demonstrate their selection. For example, c1, c2, d1, d2.
This is a good point. We will include a sensitivity analysis on the hyperparameters, justifying the choices on both simulated and real data.
In section4.8, I am confused about $ρ_j$ the experiment 2, 5, 8, 11. Why $ρ_j$ both represents ZI rate and correlation?
We apologise for the notational oversight, which will be rectified.
In Section 4.5, it is difficult to understand the sentence "for me threshold u". Besides, what is $r$ represent in Section 4.5?
We apologise for the confusing sentence. $r$ is the Pearson correlation coefficient, as explained at the start of 4.5
Why there is "(6a)Agreement between SCRaPL and Pearson" in Fig. 4?
This simply means that the panel shows a methylation/ expression scatterplot for a gene where estimation by SCRaPL and Pearson return both a significant association. We will expand the caption to explain further.
For Fig.1, I cannot see the text in the rectangle.
Apologies, we will improve the readability of the figures
I would like to see the efficiency analysis for SCRaPL.
As part of part of re-implementation in a more accessible programming language, we have preformed preliminary efficiency analysis for MCMC , demonstrating linear scalability. Results will appear in the revised manuscript.
Reviewer 2
The authors present a Bayesian model to determine noise-corrected correlation coefficients for gene expression (RNA) and DNA-methylation data at single-cell resolution. The authors present a series of simulation data and an example of matched multi-omics data, and compare their results with Pearson correlation. Noise modelling allows the model to determine gene-methylation correlation patterns more accurately. While the authors demonstrate a neat application on accurate quantification of correlation coefficients, I see a limited use of the model for the broader single-cell community. The authors may therefore improve their manuscript on several aspects.
We thank the reviewer for the encouraging words, and thank him/ her for the critical observations, which we have taken at heart, considerably broadening the scope of our paper to make it more attractive to a larger community.
- Abstract: please specify the omics layers that you are analyzing (RNA + DNA methylation) in the abstract
We acknowledge that, while SCRaPL is potentially general, in the first submission we focused only on RNA and DNA methylation. We have now decided to expand our analyses to include 10X data of simultaneous chromatin accessibility (ATAC-seq) and RNA.
- What is the benefit of using a Bayesian model formulation in this setting?
The benefit is twofold: a principled treatment of noise, and a quantification of the resulting uncertainty which allows for a meaningful way to compute Bayesian significance levels. We will expand the discussion of the relative merits of a Bayesian vs frequentist approach.
- Does it also apply to unmatched data?
In principle, given measurements with the same number of cells in all modalities, it is possible to apply SCRaPL. However, unless there is a natural pairing between different cells, the scaling of this approach will be quadratic in the number of cells, hence potentially expensive (although largely parallelizable). We will discuss this now, particularly in the light of applying SCRaPL in conjunction with other suites such as Seurat.
- Would SCRaPL allow for differential correlation testing?
At the moment, SCRaPL does not allow for differential correlation testing. Of course, one may run SCRaPL separately on two groups of cells and compare the resulting estimates, which would be informative. Nevertheless, extending SCRaPL to perform differential correlation testing (e.g. using Bayesian model selection) would be a non-trivial effort. We will add a comment on this issue to the discussion section.
- Figure 1: The graphical description of the model is rudimentary. I believe that the model description could profit from a graphical model representation of SCRaPL (as presented in figure 5).
We will redraw Fig. 1 and incorporate the graphical model from Fig 5.
- Simulated data: all experiments seem to have rather low cell numbers (max. 200) and genes (max. 300). Given that 10X Genomics is the most widely-used sequencing platform with approx. 10,000 cells and 3,000 (highly variable) genes per experiment, and given that the authors show a use-case with 9480 genes in 487 cells, it seems appropriate to extend the simulations and runtime estimates of the presented model to several thousands of cells and genes, respectively.
Thank you for this comment. The original simulation settings were designed with scMT data in mind, where indeed only a few hundred cells can be assayed at most. Partly because of this feedback, and also because of the request of implementing SCRaPL in a different language, we are working on a more scalable Tensorflow implementation which will be able to handle thousands of cells and genes in a matter of tens of minutes . The new simulated data will therefore extend into this regime with larger data sets.
- Figure 4: Please revise the figure legend as I did not understand the plotted results based on the description.
We will do so.
- Results section 2.5: Please formulate your whole argument about epigenetic regulators. I do not think that "For further information please refer to supplementary figure XYZ." Is an appropriate closing statement for a paragraph, nor does it motivate the reader to look at the supplementary figures (I did look at them and I do not see how they support the point made in the paragraph). Please elaborate and consider a "take home message" for the paragraph such that the reader is able to understand the benefit of SCRaPL without revisiting the original data publication.
Thank you for this pointer, we will take it on board in the full revision.
- Conclusion: The authors mention that SCRaPL would further offer a "template for the application of more complex analysis techniques (such as clustering, dimensionality reduction and network inference)". If that was the case, the authors should consider a comparison to other tools, which offer exactly that (e.g. Seurat's CCA or non-negative matrix factorization in LIGER). Further, the authors should set their work into context with tools like bindSC.
Thank you for the suggestion. As far as we can tell, all of these methods are thought for unmatched data, rather than multi-omics assays performed in the same cells. Having said that, it is in principle possible to “preprocess” data with SCRaPL and then feed to Seurat or other tools the latent means computed by SCRaPL. We will include an example of how this may be done in the revision.
- Implementation: Matlab is used in about 6% of the single-cell RNAseq tools (according to scrna-tools.org). To reach a larger scientific community, do the authors plan to provide an R or Python implementation of their model?
We are now implementing SCRaPL in Python using Tensorflow probability, hoping to achieve substantial speedups (see response to previous point).
Additional minor points about formatting by Reviewer 2 will all be addressed.
Reviewer 3
Maniatis et al propose a sound strategy to analyse single-cell multi-comic data sets. A key advance is to use bespoke error models for each of the omics data. These are integrated into a multivariate gaussian model. This method is a novel and, in my opinion, a valuable addition to the analyses of the growing multi-omics single-cell data sets.
We thank this reviewer for his/ her appreciation of our work.
- Authors make a convincing argument of the importance of principle methods and in particular to use noise models that tailored to the data at hand. To further support this, can authors elaborate on how results would be different from using commonly applied methods ? Eg those embedded in the Seurat, OSCA, and scanpy 'suites'? Authors compare to Pearson correlation-based methods but is not clear if that is the true state-of-the-art on those methods
As far as we know, volcano plots of p-value versus Pearson correlation are the most commonly employed approaches to assess correlations amongst different molecular modalities in single-cell multi-omics (see e.g. Argelaguet et al, Nature 2020). Seurat and other methods normally do not deal with single-cell multi-omics (i.e., multiple omics measured in the same cell), rather with multiple single-cell omics (different molecular modalities assayed in different cells). Nevertheless, it is possible to pre-apply SCRaPL to non-matched data and then use another suite; as an illustration, we will perform an analysis on scMT data using SCRaPL followed by Seurat.
- In the case study on mouse embryonic stem cells, authors excluded the chromatic accessibilty. Why not using it to more clearly show the value of the method?
We did use SCRaPL also on chromatin accessibility, however the signal was weaker and we did not include it in the manuscript, we will now present these results as supplementary material.
- It would also be great if authors would use a different single-cell multi-comic data sets, using other dat modalities, e.g. CITE-Seq data. If this not possible, at least they should elaborate on which omics SCRAPL can handle, what would be the noise models for different data types, etc.
We have started analysing a joint scATAC-scRNA- seq data set generated using the new 10X commercial platform, and will add the results of this analysis to the revised manuscript. We will also expand the description of the suitability for different data types.
*- As the authors acknowledge, computational burden is high, which presumably limits scalability. Are authors able to further explore this (scalability on Insilico data)? Or how complex is adopting the variational inference method suggested? I appreciate that the variational inference implementation might be out of the scope of this paper, though.
- It is a pity that the method is in Matlab. Nearly no-one in single-cell omics use Matlab. Our own lab is largely invested in this topic and we do not even have Matlab licenses. I strongly encourage authors to implement their method in e.g. R or python, ideally compatible with the broadly used 'suites' (Seurat, OSCA, and scanpy,...).*
We are addressed these two comments jointly by re-implementing SCRaPL in Tensorflow probability (Python based), which allow us to leverage powerful libraries for variational inference. We hope that this will lead to a substantial increase of scalability, providing the possibility of running on thousands of cells / genes in under one hour (results will appear in ).
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Referee #3
Evidence, reproducibility and clarity
Maniatis et al propose a sound strategy to analyse single-cell multi-comic data sets. A key advance is to use bespoke error models for each of the omics data. These are integrated into a multivariate gaussian model. This method is a novel and, in my opinion, a valuable addition to the analyses of the growing multi-omics single-cell data sets.
I have some comments below that I hope are helpful for the authors:
- Authors make a convincing argument of the importance of principle methods and in particular to use noise models that tailored to the data at hand. To further support this, can authors elaborate on how results would be different from using commonly applied methods ? Eg those embedded in the Seurat, OSCA, and scanpy 'suites'? Authors compare to Pearson correlation-based methods but is not clear if that is the true state-of-the-art on those methods
- In the case study on mouse embryonic stem cells, authors excluded the chromatic accessibilty. Why not using it to more clearly show the value of the method?
- It would also be great if authors would use a different single-cell multi-comic data sets, using other dat modalities, e.g. CITE-Seq data. If this not possible, at least they should elaborate on which omics SCRAPL can handle, what would be the noise models for different data types, etc.
Minor:
- As the authors acknowledge, computational burden is high, which presumably limits scalability. Are authors able to further explore this (scalability on Insilico data)? Or how complex is adopting the variational inference method suggested? I appreciate that the variational inference implementation might be out of the scope of this paper, though.
- It is a pity that the method is in Matlab. Nearly no-one in single-cell omics use Matlab. Our own lab is largely invested in this topic and we do not even have Matlab licenses. I strongly encourage authors to implement their method in e.g. R or python, ideally compatible with the broadly used 'suites' (Seurat, OSCA, and scanpy,...).
This also precludes checking software and reproducibility of results.
Significance
I think this is an important methodological development for the analysis of single-cell multi-comic data.
To my knowledge, it goes beyond existing methods and does so in a principled manner.
The audience is mostly bioinformaticians dealing with the analysis of this type of data, ie single-cell multi-omics.
My expertise is in the computational analysis of omics data, though less on the statistical fundaments of it. Hence, my group members and I are probable users of this method (if implemented in free software, as mentioned above).
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Referee #2
Evidence, reproducibility and clarity
Summary:
The authors present a Bayesian model to determine noise-corrected correlation coefficients for gene expression (RNA) and DNA-methylation data at single-cell resolution. The authors present a series of simulation data and an example of matched multi-omics data, and compare their results with Pearson correlation. Noise modelling allows the model to determine gene-methylation correlation patterns more accurately. While the authors demonstrate a neat application on accurate quantification of correlation coefficients, I see a limited use of the model for the broader single-cell community. The authors may therefore improve their manuscript on several aspects.
Major comments:
- Abstract: please specify the omics layers that you are analyzing (RNA + DNA methylation) in the abstract
- What is the benefit of using a Bayesian model formulation in this setting?
- Does it also apply to unmatched data?
- Would SCRaPL allow for differential correlation testing?
- Figure 1: The graphical description of the model is rudimentary. I believe that the model description could profit from a graphical model representation of SCRaPL (as presented in figure 5).
- Simulated data: all experiments seem to have rather low cell numbers (max. 200) and genes (max. 300). Given that 10X Genomics is the most widely-used sequencing platform with approx. 10,000 cells and 3,000 (highly variable) genes per experiment, and given that the authors show a use-case with 9480 genes in 487 cells, it seems appropriate to extend the simulations and runtime estimates of the presented model to several thousands of cells and genes, respectively.
- Figure 4: Please revise the figure legend as I did not understand the plotted results based on the description.
- Results section 2.5: Please formulate your whole argument about epigenetic regulators. I do not think that "For further information please refer to supplementary figure XYZ." Is an appropriate closing statement for a paragraph, nor does it motivate the reader to look at the supplementary figures (I did look at them and I do not see how they support the point made in the paragraph). Please elaborate and consider a "take home message" for the paragraph such that the reader is able to understand the benefit of SCRaPL without revisiting the original data publication.
- Conclusion: The authors mention that SCRaPL would further offer a "template for the application of more complex analysis techniques (such as clustering, dimensionality reduction and network inference)". If that was the case, the authors should consider a comparison to other tools, which offer exactly that (e.g. Seurat's CCA or non-negative matrix factorization in LIGER). Further, the authors should set their work into context with tools like bindSC.
Minor comments:
- Implementation: Matlab is used in about 6% of the single-cell RNAseq tools (according to scrna-tools.org). To reach a larger scientific community, do the authors plan to provide an R or Python implementation of their model?
- Fig. 2: Legends for mean, median and y=0 are hardly legible.
- Figure order: 6a is referenced before 4b and 4c (what about 4a?) - seems like a referencing issue as 6a is also listed in the figure legend of Figure 4.
- Figure 6: AIC histogram is difficult to make out behind the blue bars of the DIC histogram. Please adapt.
Reference:
Unbiased integration of single cell multi-omics data Jinzhuang Dou, Shaoheng Liang, Vakul Mohanty, Xuesen Cheng, Sangbae Kim, Jongsu Choi, Yumei Li, Katayoun Rezvani, Rui Chen, Ken Chen, bioRxiv, 2020 https://www.biorxiv.org/content/10.1101/2020.12.11.422014v1
Significance
Significance:
The use of a single-cell specific noise-model to infer accurate correlation coefficients for multi-omic analysis is a novel approach to assess information from DNA-methylation and RNA-sequencing data at single-cell resolution. As far as I am aware, methods like canonical correlation analysis (CCA), as used in Seurat, rely on the accuracy of Pearson correlation, yet, the authors of this manuscript made a convincing point on the devastating impact of noise from transcription and methylation levels on Pearson correlation.
Audience:
In order to address downstream analysis questions such as gene regulatory network inference, it is essential to have an accurate metric to assess the regulatory impact of methylation on gene expression at hand. However, an efficient implementation in a more common language (e.g. R, Python or C++) would be advisable to create a broader applicability of the model.
The reviewer's field of expertise: single-cell RNAsequencing, data analysis, data integration, Bayesian modelling
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Referee #1
Evidence, reproducibility and clarity
This paper proposes a noise-aware approach SCRaPL for modelling the associations of single cell multi-omic data. For gene expression, it uses Poisson-lognormal model. For DNAm data, it uses Binomial noise model which explicitly takes into account the average within the region. The Bayesian hierarchical framework employed by SCRaPL could achieve higher sensitivity and better robustness in identifying correlations, and also offer a template for the application of more complex analysis techniques to multi-omics data. The symbols of this paper are a little bit confusing, and I suggest authors to carefully check them. My comments are as following:
- The symbols used in this paper are messy. For example, "1" and "2" are subscripts in Eq.(2) but become superscripts in Figure 5. Besides, there are many symbols not explained such as mj, Hj, Ψ0, etc. Also, I don't know if x{j,i}^{(1)} , x{j,i}^{(2)} in Figure 5 are same with x{ij1} and x{ij2} in Eq.(3). There are many places mismatch, authors should check carefully.
- Why the equations in Fig.5 are totally different with Section 4.2? For example, pj ∼Beta(αj ,βj ) in Fig.5 but ρj ∼ Beta−1,1 in Eq.(8).
- The paper involves a lot of hyper-parameters which doesn't demonstrate their selection. For example, c1, c2, d1, d2.
- In section4.8, I am confused about $ρ_j$ the experiment 2, 5, 8, 11. Why $ρ_j$ both represents ZI rate and correlation?
- In Section 4.5, it is difficult to understand the sentence "for me threshold u". Besides, what is $r$ represent in Section 4.5?
- Why there is "(6a)Agreement between SCRaPL and Pearson" in Fig. 4?
- For Fig.1, I cannot see the text in the rectangle.
- I would like to see the efficiency analysis for SCRaPL.
Significance
Audience who interested in multi-omic data, single-cell rna, machine learning will be interested in this paper.
My field of expertise: machine learning, single-cell RNA
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Reply to the reviewers
First of all, we would like to thank the editor and all reviewers for the effort to evaluate our paper in this difficult era of COVID-19.
Reviewer #1
(Significance): Overall, this manuscript is very clear and easy to follow. The manuscript could be improved by making the following changes:
We thank the reviewer for the favorable comment and will revise the manuscript according to the suggestions.
Reviewer #2
(Evidence, reproducibility and clarity): The use of genetics is particularly impressive but the lack of major discoveries dampens the enthusiasm. Additional efforts to mechanistically define wave initiation and wave propagation would significantly improve the impact of the manuscript. Moreover, some of the conclusions are not fully supported by the data and require further experimentation and/or analysis.
We admit that marked redundancy of function among the EGFR ligands and their essential roles in cell growth prevent us from obtaining very clear results. Considering the importance of EGFR ligands in biology, we believe, our observation will give invaluable suggestions to whom wishes to clarify the roles played by EGFR-family protein in other biological contexts.
(Significance): While it is known that ADAM17 is critical to process EGFR ligands, the specific or redundant roles of different ligands remains an open question. The authors find that all ADAM17 ligands contribute to ERK signaling waves but may have specific contributions to other phenotypes. This work would be of interest to the signaling dynamics, epithelial and developmental biology communities.
We thank the reviewer for the favorable comment.
Reviewer #3
(Evidence, reproducibility and clarity): Overall, this study is carried out with a high degree of rigor and technical excellence, with clear reporting of experimental details and replication. The writing and figures are very clear, and there are no obvious technical problems. However, there are some areas in which the strength and clarity of the conclusions could be strengthened by relatively simple experiments.
We thank the reviewer for the favorable comment. We have already performed some of the experiments suggested by the reviewer. As the reviewer might have anticipated, co-culture with the wild type MDCK cells helps mutant cells to survive. We believe we could propose a clearer model in the revised paper.
(Significance): This study definitively establishes the role of 4 EGFR ligands in the generation of ERK activity waves in MDCK cells. While other studies, including some from the senior author's lab, have strongly indicated that EGFR autocrine signaling is important for these waves, this study goes further in comparing the roles of these ligands using knockouts to unambiguously establish the autocrine factors involved. Others who use this common experimental system (MDCK) to study epithelial dynamics will find this study of great interest. A wider audience of those who work on EGFR-mediated signaling will also find the data quite fascinating as an example of the complex relationship between ERK activation and its downstream effects. The technical excellence of the paper will make it a must-read for those in these fields. However, there are some factors that limit the scope of the significance. MDCK cells are an important experimental model system but differ in substantial ways from other epithelial cells, particularly in the expression of EGFR ligands. Because different ligands such as amphiregulin dominate in other systems (as noted by the authors, and PMID 27405981), the ability to extrapolate from these findings to other cell types is somewhat limited. Also, the paper avoids addressing the major question of how ERK waves relate to collective migration rate. From the data presented it is clear that this relationship is complex; for example, bath application of the ligands restores a high migration rate but not ERK waves. Given this lack of a clear relationship it is an understandable decision to leave this question for future work; however this does limit the conclusions that can be drawn from the study.
We completely agree with the reviewer’s view. It is uncertain to what extent the observation with MDCK cells can be generalized to other cell types. We also admit that the conclusion is not very simple because EGFR signaling is required for various cellular functions including cell survival and migration. Even though the gene editing becomes so easy, it is still labor consuming work to knock out many genes in a single cell line with extensive characterization. We believe the data shown in our work will provide a basis for the understanding of EGFR ligands.
Reviewer #1
For Fig 1F, 3 individual experiments should be conducted to confirm results.
We will follow the reviewer’s suggestion and repeat the experiment.
For Fig 1G, could the authors please show the original western blot data in full rather than just the densitometry graphs?
We did not show just for the sake of brevity. We are happy to will include the images as a supplementary data.
The authors should explain the origin/phenotype of MDCK cells for those who are not familiar with the cell line.
We will modify the text according to the reviewer’s suggestion.
The authors should give a future outlook/direction for future experimentation to further confirm redundancy in EGF ligands in the propagation of ERK activation waves.
We will discuss on the redundancy in other cell types based on available NGS data.
Some mention of the use of biosensors in the abstract and introduction is recommended as this is a major part of the experimental work.
We will refer to the biosensors in the abstract and introduction.
Reviewer #2
There are conflicts with some of the conclusions made about ligands. dEGFR cells have basal ERK activity as high as WT which argues against EGF being responsible for basal ERK activity. Further, basal ERK activity was not rescued by restoration of EGF in the 4KO-EGF cells. The authors should address this discrepancy.
We agree that some new questions have arisen from our observations. The discrepancy of the phenotypes between dEGFR cells and dEGF cells is an example. We are currently establishing dEGF cell lines, in which different genomic sequences of the EGF gene were targeted. We have already started to develop these cell lines and will obtain them within a month. The result will provide some clues to answer the questions. However, even if we could not solve the question, we believe, it is worth reporting observations that could not be easily understood, because such questions are often leading to another discovery.
Besides the ones genetically disrupted in this work, other EGFR ligands seem to play functional roles given that dEGFR cells less migration and fewer ERK waves than 4KO cells. The authors could test if other ligands are upregulated in 4KO cells to compensate. On a similar note determining whether ADAM17 deficient cells are more similar to 4KO cells or dEGFR cells could provide some insight.
According to the reviewer’s suggestion, we will conduct qPCR of growth factors in mutant cell lines to see the expression levels of seven EGFR ligands might have changed significantly. At the same time, as the reviewer suggested, we will establish ADAM17 knockout cell lines and compare the phenotype with those of cell lines deficient from EGFR ligand genes.
- The authors propose that Nrg1 is responsible for ERK waves in QKO, 4KO, dEGFR, and 4KO-EGF cells but are limited in testing this due to Nrg1 being essential in 4KO cells. First, Nrg1 should have been deleted in TKO cells to confirm that it is only essential in the absence of the four EGFR ligands. Additionally, Nrg1 could be knocked out in 4KO-EGF cells to demonstrate the claim that EGF-induced ADAM17 cleavage of Nrg1 is responsible for ERK waves.*
We do not think the deletion of Nrg1 in the TKO cells will abolish the ERK activation waves because EREG in TKO cells could transmit the waves. To overcome the problem of cell growth, we will try to obtain 5KO cells by Cre-induced deletion of NRG1 in 5KO-loxP-NRG1 cells, wherein EGF is supplied exogenously. We already had preliminary data suggesting that co-culture with wild type MDCK cells helps 5KO cells grow.
The authors state that ERK activation waves are important for collective migration and seek to understand the roles of each EGFR ligand, but despite measuring migration and properties of ERK activity, there is very little analysis or commentary on the relationship between the two. The ability of HB-EGF to restore migration without ERK waves suggests that waves are not required per se. It is interesting to note that with restoration of ligands, migration is higher than WT but ERK activity is lower.
We refrained from spending much space about the essential role of ERK activation waves in collective cell migration, because several papers have already described this issue.
Probably, we should have spent more space to emphasize that the collective cell migration is comprised of at least two different phenomena. The migration of leader cells and the follower cells. The ERK activation waves are essential for the follower cells but not the leader cells. In 4KO cells, both the leader cell and follower cell migrations are impaired. We showed that GFs expression restore the leader cell migration, but not the follower cells. We will revise the text to include this issue.
It is suggested that the total amount of EGFR ligands may be the primary determinant of migration, but deletion of TGFα alone causes a significant decrease in migration comparable to the DKO cells. TGFα has the lowest expression of the four ligands studied but is the only ligand to have a significant impact on migration in the single knockout context, which disagrees with that conclusion.
Each EGFR ligand has different affinity to EGFR, which makes it difficult to link the mRNA levels directly to the effect of each EGFR ligand. We will modify the discussion to include this argument.
Other:
Fig. S3B needs clarification that the WT (black) and 4KO (green) did not receive a stimulus.
We will follow the reviewer’s advice.
Reviewer #3:
The experiments in Fig. 5 are undertaken with the purpose of assessing whether NRG acts as an additional ligand that mediates the residual ERK waves in 4KO/QKO cells. However, this question is never addressed in the NRG/4KO cells. While it might be challenging due to the proliferative defect, it seems important to attempt this experiment in some way; measuring the ERK waves for these cells would establish whether all of the critical autocrine factors have been identified. Can the proliferation be rescued by application of high amounts of growth factors?
This question is similar to a question raised by reviewer #2.
To overcome the problem of cell growth, we will try to obtain 5KO cells by Cre-induced deletion of NRG1 in 5KO-loxP-NRG1 cells, wherein EGF is supplied exogenously.
The bath exposure to EGFR ligands shown in Fig. S3A is an important experiment, but it is surprising that ERK signaling is not maintained under these conditions. Is this due to depletion of the added ligands, perhaps locally? Or is the intermittent nature of paracrine signaling needed to maintain ERK activity? These possibilities could be distinguished by checking whether the added EGF or the other ligands are depleted after several hours, or by restimulating with a new bolus of ligand after several hours.
We thank the reviewer for this invaluable suggestion. We will conduct the experiments suggested by the reviewer.
The connection between ERK activity and migration is somewhat confusing. It would be helpful to show the dose sensitivity of migration to a MEK or ERK inhibitor. Are other pathways downstream of EGFR such as PI3K involved in the autocrine-mediated migration? This could also be established with the appropriate inhibitors.
We should have spent more space to emphasize that the collective cell migration is comprised of at least two different phenomena. The migration of leader cells and the follower cells. The ERK activation waves are essential for the follower cells but not the leader cells. In 4KO cells, both the leader cell and follower cell migrations are impaired. We showed that GFs expression restore the leader cell migration, but not the follower cells. We will emphasize this issue in the revised manuscript.
Reviewer #1:
Line 47 in Abstract should read "Aiming for" not "Aiming at".
We have corrected the mistake as suggested.
Some in the field call fluorescence lifetime microscopy "FLIM", you could adopt the same wording in your manuscript to attract more readers.
We have included FLIM according to the reviewer’s suggestion.
Reviewer #1 :
Figure 1D, the images should be presented using the same scale for both the EKAREV and EKARrEV constructs so that they can be directly compared.
Because the basal FRET/CFP ratio is significantly different between EKAREV-NLS and EKARrEV-NLS, the changes during mitosis become unclear if we applied the same scale. This figure is prepared to show the reactivity to Cdk1 during mitosis; therefore, we believe the current scale is better for presentation.
The names QKO and 4KO are a bit confusing. Could the authors please change the naming of the knockout cells so that readers understand that QKO and 4KO are two separate cell types? Perhaps instead of 4KO use FKO for "full knockout" or something similar. The 5KO line might also need to be named something else if you change to FKO.
We have discussed this issue with the co-authors, but could not reach a better idea. Instead of changing the names, we will include a detailed explanation for each cell line.
Reviewer #2:
The interpretation of the RA-SOS coculture experiments is confusing. Based on the author's reasoning, I would expect ADAM17 shedding in the RA-SOS cells to trigger signaling at the interface of both WT and 4KO cells but the 4KO should be unable to propagate the wave farther away from the interface. This does not seem to be the case. Do RA-SOS ADAM17KO cells still trigger waves of ERK signaling in the WT cells? Do ADAM17KO cells behave as the 4KO cells in this coculture system?
Probably, the reviewer misunderstood the method. The GF-less 4KO cells were co-cultured with wild type cells harboring the RA-SOS system. We will describe more in detail to avoid misunderstanding.
Finally, the growth curve in Fig. 5B indicates that 5KO-loxP-NRG1-CreERT2 cells are viable for about two days after Cre induction. The authors could perform a confinement release assay of these cells 1-1.5 days after Cre induction to look for further reduction of ERK waves and migration to demonstrate the role of Nrg1.
This experiment may not be necessary. It is clear that NRG1 is required for the survival of 4KO cells. The reason why cells are still alive 1 to 2 days after 4-OHT application is simply because NRG1 protein is remaining. The interpretation of the results would be difficult during the phase of NRG1 reduction.
In Fig. 1G, the normalization of all WT pERK samples to 1 artificially lowers the variance to zero when performing the T-test.
For the comparison of immunoblotting data derived from independent experiments, the signals must be normalized to the control. We believe the use of pERK/ERK of the wild type cells as the control is reasonable for this experiment.
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Referee #3
Evidence, reproducibility and clarity
This manuscript seeks to clarify the mechanisms that underlie traveling "waves" of ERK activity that occur in monolayers of migrating epithelial cells. A combination of live cell imaging with ERK activity biosensors and CRISPR-mediated knockouts for autocrine regulators are used to dissect the factors that make these waves possible. The authors utilize the MDCK cell line, which shows very prominent wave behavior, and they perform an impressive number of knockouts to eliminate the most abundant autocrine EGFR ligands. They also introduce a novel ERK FRET reporter, which is less sensitive to off-target phosphorylation by Cdk1. Analysis of ERK biosensor data from the knockouts shows that knockout of all four main EGFR ligands is needed to substantially reduce the amplitude of ERK waves, although it does not completely eliminate it. Re-expression of any of the four ligands, with the exception of HBEGF, restores strong ERK waves. Application of the same ligands in solution restores migration but not the ERK waves.
Overall, this study is carried out with a high degree of rigor and technical excellence, with clear reporting of experimental details and replication. The writing and figures are very clear, and there are no obvious technical problems. However, there are some areas in which the strength and clarity of the conclusions could be strengthened by relatively simple experiments.
Major:
- The experiments in Fig. 5 are undertaken with the purpose of assessing whether NRG acts as an additional ligand that mediates the residual ERK waves in 4KO/QKO cells. However, this question is never addressed in the NRG/4KO cells. While it might be challenging due to the proliferative defect, it seems important to attempt this experiment in some way; measuring the ERK waves for these cells would establish whether all of the critical autocrine factors have been identified. Can the proliferation be rescued by application of high amounts of growth factors?
- The bath exposure to EGFR ligands shown in Fig. S3A is an important experiment, but it is surprising that ERK signaling is not maintained under these conditions. Is this due to depletion of the added ligands, perhaps locally? Or is the intermittent nature of paracrine signaling needed to maintain ERK activity? These possibilities could be distinguished by checking whether the added EGF or the other ligands are depleted after several hours, or by restimulating with a new bolus of ligand after several hours.
Minor (I think this is an important point overall, but it is outside of the scope of the paper as defined by the authors, which is focused on the ERK waves rather than how the waves relate to migration):
- The connection between ERK activity and migration is somewhat confusing. It would be helpful to show the dose sensitivity of migration to a MEK or ERK inhibitor. Are other pathways downstream of EGFR such as PI3K involved in the autocrine-mediated migration? This could also be established with the appropriate inhibitors.
Significance
This study definitively establishes the role of 4 EGFR ligands in the generation of ERK activity waves in MDCK cells. While other studies, including some from the senior author's lab, have strongly indicated that EGFR autocrine signaling is important for these waves, this study goes further in comparing the roles of these ligands using knockouts to unambiguously establish the autocrine factors involved. Others who use this common experimental system (MDCK) to study epithelial dynamics will find this study of great interest. A wider audience of those who work on EGFR-mediated signaling will also find the data quite fascinating as an example of the complex relationship between ERK activation and its downstream effects. The technical excellence of the paper will make it a must-read for those in these fields. However, there are some factors that limit the scope of the significance. MDCK cells are an important experimental model system but differ in substantial ways from other epithelial cells, particularly in the expression of EGFR ligands. Because different ligands such as amphiregulin dominate in other systems (as noted by the authors, and PMID 27405981), the ability to extrapolate from these findings to other cell types is somewhat limited. Also, the paper avoids addressing the major question of how ERK waves relate to collective migration rate. From the data presented it is clear that this relationship is complex; for example, bath application of the ligands restores a high migration rate but not ERK waves. Given this lack of a clear relationship it is an understandable decision to leave this question for future work; however this does limit the conclusions that can be drawn from the study.
Areas of expertise: growth factor signal transduction, biosensors, quantitative modeling
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Referee #2
Evidence, reproducibility and clarity
Lin et al. address the mechanisms underlying ERK signaling waves in epithelial cells. While it is known that ADAM17 is critical to process EGFR ligands, the specific or redundant roles of different ligands remains an open question. First the authors generate a modified ERK FRET sensor with reduced cross-reactivity to CDK1 in MDCK cells and systematically knockout EGF, HBEGF, TGF⍺ and EREG (the highest expressed ligands in MDCK cells). The authors use live cell imaging of ERK activity upon release from confinement and find that all ligands contribute to ERK signaling waves. While differences in basal signaling and other dynamic features are found in individual knockouts, only the quadruple KO cells show a significant decrease in ERK waves. To determine if the 4KO cells are defective in wave propagation (as opposed to wave initiation), the authors coculture 4KO cells with an inducible cell line and conclude that 4KO cells are unable to propagate waves. Individual EGFR ligands are then restored in 4KO cells, and EGF, TGFα, and EREG, but not HBEGF, can rescue ERK activity waves. Finally, the authors attempt to eliminate all ERK activation waves by deletion of Nrg1 but find that it is essential in 4KO cells. The paper is well-written and technically sound. The use of genetics is particularly impressive but the lack of major discoveries dampens the enthusiasm. Additional efforts to mechanistically define wave initiation and wave propagation would significantly improve the impact of the manuscript. Moreover, some of the conclusions are not fully supported by the data and require further experimentation and/or analysis.
- There are conflicts with some of the conclusions made about ligands. dEGFR cells have basal ERK activity as high as WT which argues against EGF being responsible for basal ERK activity. Further, basal ERK activity was not rescued by restoration of EGF in the 4KO-EGF cells. The authors should address this discrepancy.
- Besides the ones genetically disrupted in this work, other EGFR ligands seem to play functional roles given that dEGFR cells less migration and fewer ERK waves than 4KO cells. The authors could test if other ligands are upregulated in 4KO cells to compensate. On a similar note determining whether ADAM17 deficient cells are more similar to 4KO cells or dEGFR cells could provide some insight.
- The interpretation of the RA-SOS coculture experiments is confusing. Based on the author's reasoning, I would expect ADAM17 shedding in the RA-SOS cells to trigger signaling at the interface of both WT and 4KO cells but the 4KO should be unable to propagate the wave farther away from the interface. This does not seem to be the case. Do RA-SOS ADAM17KO cells still trigger waves of ERK signaling in the WT cells? Do ADAM17KO cells behave as the 4KO cells in this coculture system?
- The authors propose that Nrg1 is responsible for ERK waves in QKO, 4KO, dEGFR, and 4KO-EGF cells but are limited in testing this due to Nrg1 being essential in 4KO cells. First, Nrg1 should have been deleted in TKO cells to confirm that it is only essential in the absence of the four EGFR ligands. Additionally, Nrg1 could be knocked out in 4KO-EGF cells to demonstrate the claim that EGF-induced ADAM17 cleavage of Nrg1 is responsible for ERK waves. Finally, the growth curve in Fig. 5B indicates that 5KO-loxP-NRG1-CreERT2 cells are viable for about two days after Cre induction. The authors could perform a confinement release assay of these cells 1-1.5 days after Cre induction to look for further reduction of ERK waves and migration to demonstrate the role of Nrg1.
- The authors state that ERK activation waves are important for collective migration and seek to understand the roles of each EGFR ligand, but despite measuring migration and properties of ERK activity, there is very little analysis or commentary on the relationship between the two. The ability of HB-EGF to restore migration without ERK waves suggests that waves are not required per se. It is interesting to note that with restoration of ligands, migration is higher than WT but ERK activity is lower.
- It is suggested that the total amount of EGFR ligands may be the primary determinant of migration, but deletion of TGFα alone causes a significant decrease in migration comparable to the DKO cells. TGFα has the lowest expression of the four ligands studied but is the only ligand to have a significant impact on migration in the single knockout context, which disagrees with that conclusion. Other:
- In Fig. 1G, the normalization of all WT pERK samples to 1 artificially lowers the variance to zero when performing the T-test.
- Fig. S3B needs clarification that the WT (black) and 4KO (green) did not receive a stimulus.
Significance
While it is known that ADAM17 is critical to process EGFR ligands, the specific or redundant roles of different ligands remains an open question. The authors find that all ADAM17 ligands contribute to ERK signaling waves but may have specific contributions to other phenotypes. This work would be of interest to the signaling dynamics, epithelial and developmental biology communities.
-
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Referee #1
Evidence, reproducibility and clarity
see below for comments.
Significance
Overall, this manuscript is very clear and easy to follow. The manuscript could be improved by making the following changes:
- Line 47 in Abstract should read "Aiming for" not "Aiming at".
- Some mention of the use of biosensors in the abstract and introduction is recommended as this is a major part of the experimental work.
- The names QKO and 4KO are a bit confusing. Could the authors please change the naming of the knockout cells so that readers understand that QKO and 4KO are two separate cell types? Perhaps instead of 4KO use FKO for "full knockout" or something similar. The 5KO line might also need to be named something else if you change to FKO.
- Figure 1D, the images should be presented using the same scale for both the EKAREV and EKARrEV constructs so that they can be directly compared.
- Some in the field call fluorescence lifetime microscopy "FLIM", you could adopt the same wording in your manuscript to attract more readers.
- For Fig 1F, 3 individual experiments should be conducted to confirm results.
- For Fig 1G, could the authors please show the original western blot data in full rather than just the densitometry graphs?
- The authors should explain the origin/phenotype of MDCK cells for those who are not familiar with the cell line.
- The authors should give a future outlook/direction for future experimentation to further confirm redundancy in EGF ligands in the propagation of ERK activation waves.
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
**Summary:**
Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate). Please place your comments about significance in section 2.
In this paper the authors used a targeted approach to identify rare mutations in a cohort of glioma patients. Using this approach they identified a recurrent mutation in the TOP2A gene encoding for Topoisomerase 2A, and suggest that this mutation creates a more effective protein, binding DNA strongly and maybe more enzymatically active. RNAseq analysis of TOP2A WT and TOP2A mut tumor samples suggest different transcription patterns and points to possible splicing defects. The most recurrent variant (E9448Q) is described in depth and some experimental information shows this variant might be a gain-of-function mutation.
**Major comments:**
Are the key conclusions convincing? The validation of both the methodology and the presence of never described TOP2A variations in HGG is done quite successfully. Interesting evidence about relevance of the most frequent mutation is provided. However, besides having computational and biochemistry assays performed, lack of details about in vitro experiment statistics (no p-values are provided in figures 4 and 5, neither sample size, repetitions) weakens the conclusions claimed by the authors about the properties of the mutated topoisomerase. Ad. In the revised version we provided more details about in vitro experiments, including statistics when is applicable, sample size and a number of repetitions. In the fig. 4 we show the results of two repetitions (so we can’t calculate statistics) but I would like to stress that we tested independently two fragments of the protein and the results were similar, so our conclusion was justified. However, we do agree with the reviewer that a statistical analysis of those biochemical tests is required. We already started to produce a new batch of recombinant proteins and we will add repetitions to reinforce our claims. We will provide statistical analysis details once all experiments are performed. __
Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? Claims about E948Q variant function should be revised. Data is not presented in a convincing way, plus there is ambiguous language used from the results ("We conclude that the E9448Q TOP2A protein is functional, and MIGHT have a higher activity than the WT protein") to the rest of the paper where they strongly support the claims about the TOP2A activity. Ad. We will provide more data on biochemical features of the TOP2A variant to confirm the impact of the E948Q substitution on enzyme activities, which would allow more strong conclusions. This will present our results in more convincing way. A language of the manuscript has been critically revised and modified (see a version with tracked changes).
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. In line with the presented data in the paper, additional experiments that show catalytic changes of the E9448Q variation must be added. It is shown that there are differences in the DNA binding capacity by EMSA compared to the WT form, however, the DNA supercoil relaxation activities is not that different, at least the way the results are presented. The authors suggest that TOP2A mutation is a driver mutation but no validation in vitro of this claim is shown. Can this mutation alone or in combination with e.g. tumor suppressors transform normal cells to cancer cells? Do cell lines expressing this mutation (compared to parental TOP2A wt expressing cells) display increased transcription? Increased invasion? Ad. In the revised version we moderated our conclusions and we do not state that the mutated TOP2A is an oncogenic driver. We suggest this mutation (and possibly other TOP2A mutations, as we analyzed the impact of other variants on the TOP2A protein function) contribute to gliomagenesis. This conclusion is based not only on the changes in biochemical properties, but also on the observation of the impact of the mutation of transcription and patient survival. We expanded the analysis of TOP2A mutations and expression levels on TCGA datasets and those new results support our conclusions about a pathogenic nature of TOP2A overexpression and mutations (the supplementary fig.4). We believe in such situation, there is no rationale to make a classical oncogenic driver experiment.
Due to a rarity of the TOP2A mutations it is impossible to find a patient derived cell line with such defect. We attempted to overexpress TOP2A in glioma cells but apparently there is some autoregulation preventing overexpression of this protein is cells with endogenous TOP2A expression. Therefore, we can’t verify if cell lines expressing this variant (compared to parental TOP2A wt expressing cells) have increased transcription. Moreover, such experiments are costly and require more time investment for substantial experiments
I would like to stress that modeling some events in cell cultures is difficult and we found in GBMs the link between the mutated TOP2A and increased transcription along with decrease of splicing factors expression.
We have attempted to make CRISPR/Cas9 mediated knock-in in glioma cells but without success. This is a difficult and time consuming procedure. Although in principle, we agree on the rationale for such experiment, we think that the current data are consistent and convincing. If reviewers find it necessary we may attempt to create glioma cell lines with TOP2A knock-out and overexpression of the mutated TOP2A gene and study it functionally, but it would require more time.
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. If the authors can complement the already presented in vitro experiments with additional ones supporting their hypothesis, this should be feasible. The authors can use patient derived glioma cells or glioma cell lines manipulated to express either the parental TOP2A wt enzyme or the identified mutated form. __Ad. Due to a rarity of the TOP2A mutations it is impossible to find a patient derived cell line with such defect. Our findings partly relied on frozen historical samples, so it is not possible to develop patient-derived cell lines. As mentioned above, we can create a TOP2A knock-out cell line and overexpress a wild type or mutated version but there is no certainty that TOP2A deficient cells would survive (this is an essential enzyme) and such manipulation would be feasible.__
Are the data and the methods presented in such a way that they can be reproduced? Yes, the authors provide a quite detailed explanation of the methods implemented to reach each one of the results they are presenting.
Are the experiments adequately replicated and statistical analysis adequate? No, there is no information about the statistical analysis or number of replicates in any of the in vitro experiments performed. This information should be added to the manuscript.
Ad. In the revised version the requested information was added where was possible and additional repetitions for biochemical experiments are currently in progress.
**Minor comments:**
- Specific experimental issues that are easily addressable.
- Are prior studies referenced appropriately? Yes, authors clearly address the state of the art regarding previous NGS methodologies and let us know the advantages and novelty of their approach.
Are the text and figures clear and accurate? There are some discrepancies between the strength of the language used in different sections of the paper to refer the conclusions they can infer from the results they are showing. While they are all valid, authors should revise it. Ad. The text of the manuscript has been unified and revised.
Do you have suggestions that would help the authors improve the presentation of their data and conclusions? First of all, describe the statistical analysis used in every figure, include number of biological and technical replicates. I would also suggest to change the title or the scope of the discussion, there is too much focus on the TOP2A in the introduction, neglecting all the technical NGS work that actually lead to several new variants being described. This may be confusing when it collides with a conclusion that is heavily focused on the first half describing potential implications of at least another 3 proteins where genetic alterations were described. Given the fact there is not much experimental work that shows TOP2A mutations relevance in HGG or strong enough evidence of the variant's function I would suggest to change a bit the scope of the title. Ad. The description of the results and discussion have been revised to include additional data/discussion on technicalities and other finding not related to TOP2A. We performed additional computational analyses of TOP2A expression/mutations in the TCGA datasets. We believe that the planned experiments on genetically modified cell lines would provide additional support for our claims. We think that in the revised version a balance between landscape/NGS content and TOP2A content is well balanced.
Reviewer #1 (Significance (Required)):
- Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. The authors describe a methodology that proved to be sensitive and specific enough in order to allow them to detect rare genetic alterations in patient glioma samples. This information could be valuable to describe new driver mutations or infer in genetic pathway alterations that could be potential therapeutic targets. As the authors state at the beginning of the paper, given the poor therapeutical approaches existing for HGG currently, information of this kind could still be highly useful and provide a better outcome to a specific cohort of patients.
On a personal note, I think there is too much speculation about how TOP2A mutations could be interesting from a biological point of view (authors referred to evidence about implications of this mutation in other forms of cancer) but since no experimental validation is provided in glioma cells, it is difficult to conclude that this enzyme gain-of-function mutation could have a relevant role in HGG and thus make these variants a potential therapeutic target. There are no experiments conducted in glioma cells that express TOP2A variants, it would be interesting to see if it has an effect in the migratory/invasive phenotype like described in other cancer types or like it is suggested by analysis of the genetic pathways activated in the HGG patients samples harboring TOP2A mutation. In addition, there is no evidence of the TOP2A mutations possible role as a driver mutation, which is an interesting aspect that could be further explored from both a computational and an experimental approach.
Ad. As mentioned above, there is no glioma cells that express TOP2A variants and we are not convinced that such experiment will be feasible taking into account an essential role of TOP2A. We will attempt to perform experiments with CRISP/Cas9 knock-in cell lines and functional validation, but until now we did not accomplish knock-in in glioma cells. We will try to knock-out the endogenous TOP2A using CRISPR and express a TOP2A WT or E948Q variant from plasmids encoding these proteins, but we can’t predict if TOP2A KO cell would survive. If we manage to produce such cells, then we will investigate proliferation, migration and invasion of cells expressing TOP2A WT or mutated variant.
We do agree with the reviewer that our previous conclusions were too strong, and in the revised version we moderated our claims. We do not say that the mutated TOP2A is an oncogenic driver. We suggest this mutation (and possibly other TOP2A mutations, as we analyzed the impact of other variants on the TOP2A protein structure) contribute to gliomagenesis.
__Data on the Fig. 1A suggests that TOP2A has a mutational hotspot in the position E948Q in our dataset. In the revised version of the manuscript we have extended RNA-seq analysis of our datasets and TCGA PanCancer datasets to search for TOP2A mutations/ overexpression. We found that another computational prediction using CADD algorithm strongly confirms that TOP2A E948Q is in the top 1% of most deleterious variants in the human genome (CADD score >20). This results was added to Supplementary Table 2.__
- Place the work in the context of the existing literature (provide references, where appropriate). The quality of the paper is high and in line with other studies in the literature that perform genome and transcriptome analysis of tumor samples. It is only the experimental validation that is lacking data supporting the "in silico" findings. Ad. We would like to point that we provided the results of experimental, biochemical validation (2 assays) showing that the variant TOP2A proteins have different properties. The associations of transcriptional dysregulation in variant TOP2A bearing gliomas was not a in silico prediction but the result of the analysis of real tumor samples.
As stated above, we are ready to perform further biological validation if the editors find it necessary.
- State what audience might be interested in and influenced by the reported findings. Computational biologists are the right audience to target this paper. If additional experimental work further validating their initial bioinformatic findings is added to the manuscript then probably a wider population could be targeted.
Ad. As stated above, we are working now on providing more replicates of biochemical assays and we are ready to perform further biological validation if the editors find it necessary. I would like to stress that genome editing by knock-in is not always possible/feasible, and these type of experiments is time and money consuming.
- 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. Brain tumors, immunotherapy, cancer stem cells, tumor microenvironment, tumor heterogeneity. I do not have sufficient expertise to evaluate the bioinformatic analysis and software/programs used to analyze the NGS data.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
By exon targeted resequencing of 664 genes frequently mutated in cancer, authors identify novel mutations associated to Glioma in a cohort of 182 Polish and Canadian samples. Most of these novel mutations have been identified as potential rare germline mutations, somatic mosaicism or loss-of-heterozygosity variants. Among them, authors focus on mutations associated to the TOP2A gene, which encodes one of the two Type II topoisomerases paralogs present in humans. By a limited number of in vitro experiments, authors conclude that TOP2A recurrent variant E948Q, displays increased binding to DNA and topoisomerase activity. Therefore, authors suggest that the TOP2A E948Q variant is a gain-of-function mutation.
**Major comments:**
- Authors show an interesting plethora of new exon mutations associated with High Grade Glioma. Nevertheless, the characterization of TOP2A E948Q variant, which is the main focus of the study, although very interesting and potentially clinically relevant, remains incomplete. Association of the TOP2A E948Q glioma variant with a gain-of-function mutation would require to improve the statistical power of the presented experiments (increase number of replicates). With the existing experimental evidence, the increased DNA binding and activity of the TOP2A E948Q variant should be considered as preliminary, especially in the case of 431-1193 aa fragment. I would consider mandatory to increase experimental replicates and to analyse statistical significance in the case of DNA binding experiments and DNA relaxation assays with the TOP2A 431-1193 aa fragment. A more detailed biochemical characterization should be performed. A titration of different amounts of protein should be included in these experiments, and at least two batches of purified proteins should be analysed. Decatenation assays should also be performed to characterize the activity of the mutant protein in more detail. Recapitulation of DNA binding and activity results with other TOP2A variants obtained in this study will significantly reinforce authors claims too. This improved biochemical characterization should not take longer than two months.
Ad. We would like to stress that while two replicates are presented, we were testing two forms of TOP2A proteins and the results were similar, confirming our conclusions. But we agree that additional replicates would strengthen our claims. Therefore, we are in the process of producing another batch of recombinant proteins to increase a number of replicates and calculate statistics for the biochemical assays (binding and relaxation assay). We will perform titration of different amounts of the protein using two batches of purified proteins.
The occurrence of other TOP2A variants is low (identified in only a single patient sample), therefore we will perform experimental validation only for E948Q. However, we performed additional computational analysis for other TOP2A variants showing the influence of the substitution on DNA binding by docking the DNA fragment into TOP2A binding pocket (Supplementary table 4).
- To increase the significance of the results, I would encourage authors to include experiments showing the functional impact of this TOP2A mutation in cells. The connection with transcriptomic alterations is merely correlative, and would be greatly strengthened by functional experiments in cellular models. To draw definitive conclusions regarding the changes in transcription, I would encourage authors to complement the results with experiments that point to the physiological impact of TOP2A variants within the cell. Overexpression of WT and E948Q variants in a cell model and transcriptomic analysis would be desirable, but validation in these experimental models of some of the target genes identified as deregulated in patients could suffice. These experiments could be accomplished in no more than 3-4 months.
Ad. We agree that the connection of the TOP2A mutation with transcriptomic alterations is correlative, and would be greatly strengthened by functional experiments in cellular models. If we develop a TOP2A E948Q knock-in cell line or TOP2A KO cell line with E948Q over-expression, we are planning to evaluate transcriptomic changes on selected genes by qPCR or whole transcriptome by RNAseq. We estimate that developing a stable CRISPR/Cas9 cell line may take up to 6 months.
We provided additional results showing that the connection of the TOP2A mutation with transcriptomic alterations may be due to different expression of splicing factors (Supplementary Fig. 6).
- Some of the methods are not presented with sufficient detail. Regarding the DNA and RNA sequencing experiments, I consider necessary to specify the DNA fragmentation method, reference for the indexed adapters and ligation and amplification procedures (ligase reference, number of PCR cycles, etc). It would be helpful to clarify or reference which are the "special oligonucleotide probes" that are mentioned. Finally, a reference for the "special beads" and final amplification number of cycles is needed. The sequence of primers used for TOP2A cloning and mutagenesis should be included. The reference for the "site mutagenesis kit" used is missing. When studying the survival rate of glioma patients depending of TOP2A expression levels, it should be clarified what is considered HIGH or LOW expression (i.e: which percentiles are used).
Ad. We expanded the description of methodological aspects of DNA and RNA sequencing experiments. This description was revised and more details are provided in the revised version. Regarding cloning and mutagenesis, we added a table with primer sequences (Supplementary Table 5). We did not use any kit for cloning and mutagenesis. Standard methods and primers with modified nucleotides were used.
__We have included information about the partitioned groups in the survival analyses in the figure 2 caption. “D - Kaplan-Meier overall survival curve for patients with high (> TOP2A mRNA median expression x 1.25) or low (- There is a major concern about how the experiments are replicated and about the statistical analysis, which is inexistent in some cases. Indeed, Figures 4 and 5 do not present any statistical analysis, it is therefore hard to draw any conclusion. In Figure 4b, the results for the 890-996 aa fragment looks qualitatively clear, but this is not the case for the 431-1193 aa fragment. More replicates and statistical analysis are mandatory, together with a protein titration. The replicates should be performed with at least two independent batches of protein purifications. The individual values of each experiment should be included in the graph to provide a better understanding of experimental variability. All this also applies to Figure 5.
Ad. We will increase a number of replicates for the binding and relaxation assay. We will perform a titration of different amounts of protein in these experiments using two batches of purified proteins.
**Minor comments:**
- The effect on transcription of co-occurrence of TOP2A mutations with other mutations could also be analysed with the already available data. Also, a more detailed analysis of genome-wide transcription could also be used to at least partially address the proposed hypotheses of increased transcriptional rate or splicing aberrations.
Ad. We don’t have enough samples with the TOP2A mutation to analyze the effect on transcription of co-occurrence of TOP2A with other mutations.
We addressed the hypothesis of increased transcriptional rate or splicing aberrations by performed additional analyses of RNA-seq data to confirm splicing aberrations. Indeed we found splicing machinery genes down-regulated in the E948Q TOP2A glioma samples (Supplementary Fig.6).
- There is no reference for the following argument "As the identified germline variants were exceptionally rare in the general population ... it is likely that these variants are pathogenic". I also find low number of references to support the suggested high frequency of altered genes in gliomas compare to other cancer types. I miss specific works relating TOP2 activity with transcriptional regulation.
Ad. The appropriate references are provided to back-up these statements.
- At several points in the text there are quantitative and comparative statements that should be backed up by the actual numbers (e.g. "The results of the targeted sequencing indicate a high frequency of altered genes", "The most altered gene was TP53, followed by IDH1...", "Other genes that were found to be frequently altered included KDM6B...", "These partial results combined with a low frequency of this variant in the Polish population suggest a somatic mutation"). The same thing applies to the co-occurrence of mutations, in which the percentage of co-occurrence and significance is not indicated. This lack of detail in the description is also observed in the description of the transcriptomic alterations in which no detail is provided regarding how many of the 105 analyzed samples correspond to low or high gliomas.
Ad. We apologize that the frequencies of mutated genes were not specified. This information is included in the main text of the revised version. We now provide a gnomAD frequency for all variants of interest, confirming the low frequency in the population (AF__ __
Regarding the total number of samples in the transcriptomic analysis, we provided an updated supplementary table covering also samples that were used for transcriptomic analyses (Supplementary Table 1).
- For TOP2A mutation analysis, sometimes is not clear when the analysis is done with the 9 mutated samples and when with the 4 recurrent TOP2A E948Q variants. For example, in figure 2b and 2c analysis are done with 9 samples while the figure 2e is based on the 4 E948Q variants. At least this is what I have deduced from the main text, it should be clarified in the figure legend).
Ad. This information has been included in the captions of Figure 2B, 2C and 2E and now we specify how many samples were used in each analysis.
- Fig1. In figure 1b it would be interesting to color-code patients by glioma grade. This would also apply to Figure S1a, S1c, 2a, S3 and S4. In figure 1D it would be very informative to distinguish mutations that passed the quality control or not with different colors.
Ad. Following reviewer’s suggestions, we have added this information, and oncoplot figures derived from the germline analysis have a distinct color for each glioma grade. In the figure 1D, all of the presented mutations have passed a quality control in terms of quality of sequencing. One additional criterion that was used for all genomic results (except some of the TOP2A variants) was a criterion of 20% variant penetration (20% of reads in the position had to come from the alternative allele). We corrected the description in the Supplementary Table to “passed 20% penetration criterion”. The rationale behind this criterion for TOP2A variants was a fact that for one of the E948Q samples it was ~13% and we didn’t want to lose this sample from the analysis due to rarity of the mutation.
- Fig2. In figure 2b and 2c the statistical significance of differences between TOP2A and the rest of genotypes should be included. Looking at Figures 2d and 2e it looks surprising how similar is the overall survival of HIGH TOP2A mRNA expression (500 days, fig 2d) with the overall survival of the TOP2A WT samples (400 days, fig 2e). Here a I would include a graph that summarizes the TOP2A mRNA expression levels of each group in fig 2d and 2e.
Ad. We agree that median overall survival is similar comparing patients with high TOP2A mRNA expression to TOP2A WT patients in our cohort. It is worth noting, however, that both datasets were produced using different library protocols, and the methodology is different, so it can’t be expected the levels to be equal. We think that adding two more graphs, as suggested, would add another layer of information to this section of the analysis. We have included two boxplots depicting TOP2A mRNA RPKMs, and it is clear now that the medians of High TOP2 mRNA and TOP2A mutant (E948Q) are more closely related, despite the fact that we only have a few patients with the mutation.
- Fig3. It would be interesting to include the same simulation for the rest of TOP2A mutations as supplementary figure.
Ad. We agree that the other TOP2A SNPs could potentially affect DNA binding. We focused on the recurrent mutation and did not analyze those occurring in a single patient. In the revised version we included predictions whether these variants could affect TOP2A DNA binding. For WT TOP2A and variants, we calculated the Gibbs free energy (ΔG). This information can be found in Supplementary Table 4. We have extended description in the Results section: “The TOP2A E948Q substitution may affect protein-DNA interactions”
- Fig4 and Fig5. Include statistical analysis and dots representing individual replicates.
Ad. For Fig 4 we have two replicates for two protein fragments, so we can’t present statistics now. As mentioned above we are preparing a new batch of proteins and will make more repetitions of EMSA and relaxation assays. For Fig 5. we have 3 replicates but despite a trend there is no statistical significance. We intent to make more replicates and a separate protein preparation. After including additional repetitions we will present the results as dots representing individual replicates.
- Fig6. In Figure 6d I would increase the size differences in the dots representing the gene counts, as it is not easily perceived with current parameters.
Ad. The dot size in Fig 6d did not reflect the true meaning. To make it easier to understand, we changed a plot type to a barplot, which now represents the number of differentially expressed genes involved in each pathway.
- FigS2. In figure S2B, it would be informative to establish which dots are significatively above or below the diagonal.
Ad. The purpose of this figure was to show which oncogenic signaling pathways from TCGA cohorts were affected in our cohort. The pathway's size is a variable that is used to normalize the calculation (shown in abscissa axis in S2B). RTK-RAS and NOTCH pathways contain hundreds of genes, whereas other pathways, such as the NRF2 oncogenic pathway, contains only a few. On the other hand, we counted how many genes in each pathway in our cohort were mutated (shown in ordinate axis, S2B). We used logarithms in both axes for visualization purposes, but this has no effect on the enrichment of these pathways, which is shown in the color-coded legend.
- FigS3. How were the samples shown selected from the total?
Ad. In this plot we show only somatic variants that were found in at least two different patients. We apologize that this information was missing, and we have added it to the figure's caption.
- FigS4. I would include a line with the TOP2A mutation to have an idea of how these mutations are distributed between groups.
Ad. Based on the feedback of the reviewer, this figure has been modified and improved. A new row has been added to the figure, displaying TOP2A mutations alongside other highly frequent mutations in other genes.
Reviewer #2 (Significance (Required)):
In this work authors have identified new mutations associated to gliomas by targeted exome sequencing using an important cohort of 182 samples. Among these new mutations epigenetic enzymes and modifiers are found. These results potentially increase the repertoire of putative molecular targets for future cancer therapies. Authors focus in mutations associated to TOP2A gene, that provides stronger DNA binding and DNA relaxation capacity in vitro. Although further characterization is needed, tumours harbouring this kind of mutations could show higher level of sensitivity to TOP2 drugs, providing potentially interesting clinical implications. Although the link between TOP2A expression and cancer prognosis is well established, the relevance of specific mutations in still largely unexplored.
On one hand this work brings novelties in the field of Glioma providing a series of putative new players in the development of this type of cancer. Audience interested in basic or clinical aspects of these tumours would be a good target for this work. On the other hand, this putative gain-of-function mutation of TOP2A represent an interesting aspect for the DNA topology and topoisomerases field. Although, as stated above a more detailed biochemical and functional characterization would be required to draw the attention of this audience-
Scientifically, I have experience in the DNA topology and topoisomerases field, 3D genome organization and gene regulation. I have no experience in Gliomas or any other clinical aspect of cancer, so it is difficult for me to properly establish the potential impact of the newly discovered mutations. Technically I have no capacity to critically evaluate the aspects related to the targeted exome sequencing and the suitability of the analysis performed for mutation identification.
**Referee Cross-commenting**
I fully agree with the comments of the other reviewer, which are perfectly aligned with my own regarding the preliminary nature of the conclusions about the biochemical and functional characterization of the TOP2A mutations.
-
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Referee #2
Evidence, reproducibility and clarity
By exon targeted resequencing of 664 genes frequently mutated in cancer, authors identify novel mutations associated to Glioma in a cohort of 182 Polish and Canadian samples. Most of these novel mutations have been identified as potential rare germline mutations, somatic mosaicism or loss-of-heterozygosity variants. Among them, authors focus on mutations associated to the TOP2A gene, which encodes one of the two Type II topoisomerases paralogs present in humans. By a limited number of in vitro experiments, authors conclude that TOP2A recurrent variant E948Q, displays increased binding to DNA and topoisomerase activity. Therefore, authors suggest that the TOP2A E948Q variant is a gain-of-function mutation.
Major comments:
- Authors show an interesting plethora of new exon mutations associated with High Grade Glioma. Nevertheless, the characterization of TOP2A E948Q variant, which is the main focus of the study, although very interesting and potentially clinically relevant, remains incomplete. Association of the TOP2A E948Q glioma variant with a gain-of-function mutation would require to improve the statistical power of the presented experiments (increase number of replicates). With the existing experimental evidence, the increased DNA binding and activity of the TOP2A E948Q variant should be considered as preliminary, especially in the case of 431-1193 aa fragment. I would consider mandatory to increase experimental replicates and to analyse statistical significance in the case of DNA binding experiments and DNA relaxation assays with the TOP2A 431-1193 aa fragment. A more detailed biochemical characterization should be performed. A titration of different amounts of protein should be included in these experiments, and at least two batches of purified proteins should be analysed. Decatenation assays should also be performed to characterize the activity of the mutant protein in more detail. Recapitulation of DNA binding and activity results with other TOP2A variants obtained in this study will significantly reinforce authors claims too. This improved biochemical characterization should not take longer than two months.
- To increase the significance of the results, I would encourage authors to include experiments showing the functional impact of this TOP2A mutation in cells. The connection with transcriptomic alterations is merely correlative, and would be greatly strengthened by functional experiments in cellular models. To draw definitive conclusions regarding the changes in transcription, I would encourage authors to complement the results with experiments that point to the physiological impact of TOP2A variants within the cell. Overexpression of WT and E948Q variants in a cell model and transcriptomic analysis would be desirable, but validation in these experimental models of some of the target genes identified as deregulated in patients could suffice. These experiments could be accomplished in no more than 3-4 months.
- Some of the methods are not presented with sufficient detail. Regarding the DNA and RNA sequencing experiments, I consider necessary to specify the DNA fragmentation method, reference for the indexed adapters and ligation and amplification procedures (ligase reference, number of PCR cycles, etc). It would be helpful to clarify or reference which are the "special oligonucleotide probes" that are mentioned. Finally, a reference for the "special beads" and final amplification number of cycles is needed. The sequence of primers used for TOP2A cloning and mutagenesis should be included. The reference for the "site mutagenesis kit" used is missing. When studying the survival rate of glioma patients depending of TOP2A expression levels, it should be clarified what is considered HIGH or LOW expression (i.e: which percentiles are used).
- There is a major concern about how the experiments are replicated and about the statistical analysis, which is inexistent in some cases. Indeed, Figures 4 and 5 do not present any statistical analysis, it is therefore hard to draw any conclusion. In Figure 4b, the results for the 890-996 aa fragment looks qualitatively clear, but this is not the case for the 431-1193 aa fragment. More replicates and statistical analysis are mandatory, together with a protein titration. The replicates should be performed with at least two independent batches of protein purifications. The individual values of each experiment should be included in the graph to provide a better understanding of experimental variability. All this also applies to Figure 5.
Minor comments:
- The effect on transcription of co-occurrence of TOP2A mutations with other mutations could also be analysed with the already available data. Also, a more detailed analysis of genome-wide transcription could also be used to at least partially address the proposed hypotheses of increased transcriptional rate or splicing aberrations.
- There is no reference for the following argument "As the identified germline variants were exceptionally rare in the general population ... it is likely that these variants are pathogenic". I also find low number of references to support the suggested high frequency of altered genes in gliomas compare to other cancer types. I miss specific works relating TOP2 activity with transcriptional regulation.
- At several points in the text there are quantitative and comparative statements that should be backed up by the actual numbers (e.g. "The results of the targeted sequencing indicate a high frequency of altered genes", "The most altered gene was TP53, followed by IDH1...", "Other genes that were found to be frequently altered included KDM6B...", "These partial results combined with a low frequency of this variant in the Polish population suggest a somatic mutation"). The same thing applies to the co-occurrence of mutations, in which the percentage of co-occurrence and significance is not indicated. This lack of detail in the description is also observed in the description of the transcriptomic alterations in which no detail is provided regarding how many of the 105 analyzed samples correspond to low or high gliomas.
- For TOP2A mutation analysis, sometimes is not clear when the analysis is done with the 9 mutated samples and when with the 4 recurrent TOP2A E948Q variants. For example, in figure 2b and 2c analysis are done with 9 samples while the figure 2e is based on the 4 E948Q variants. At least this is what I have deduced from the main text, it should be clarified in the figure legend).
- Fig1. In figure 1b it would be interesting to color-code patients by glioma grade. This would also apply to Figure S1a, S1c, 2a, S3 and S4. In figure 1D it would be very informative to distinguish mutations that passed the quality control or not with different colors.
- Fig2. In figure 2b and 2c the statistical significance of differences between TOP2A and the rest of genotypes should be included. Looking at Figures 2d and 2e it looks surprising how similar is the overall survival of HIGH TOP2A mRNA expression (500 days, fig 2d) with the overall survival of the TOP2A WT samples (400 days, fig 2e). Here a I would include a graph that summarizes the TOP2A mRNA expression levels of each group in fig 2d and 2e.
- Fig3. It would be interesting to include the same simulation for the rest of TOP2A mutations as supplementary figure.
- Fig4 and Fig5. Include statistical analysis and dots representing individual replicates.
- Fig6. In Figure 6d I would increase the size differences in the dots representing the gene counts, as it is not easily perceived with current parameters.
- FigS2. In figure S2B, it would be informative to establish which dots are significatively above or below the diagonal.
- FigS3. How were the samples shown selected from the total?
- FigS4. I would include a line with the TOP2A mutation to have an idea of how these mutations are distributed between groups.
Significance
In this work authors have identified new mutations associated to gliomas by targeted exome sequencing using an important cohort of 182 samples. Among these new mutations epigenetic enzymes and modifiers are found. These results potentially increase the repertoire of putative molecular targets for future cancer therapies. Authors focus in mutations associated to TOP2A gene, that provides stronger DNA binding and DNA relaxation capacity in vitro. Although further characterization is needed, tumours harbouring this kind of mutations could show higher level of sensitivity to TOP2 drugs, providing potentially interesting clinical implications. Although the link between TOP2A expression and cancer prognosis is well established, the relevance of specific mutations in still largely unexplored.
On one hand this work brings novelties in the field of Glioma providing a series of putative new players in the development of this type of cancer. Audience interested in basic or clinical aspects of these tumours would be a good target for this work. On the other hand, this putative gain-of-function mutation of TOP2A represent an interesting aspect for the DNA topology and topoisomerases field. Although, as stated above a more detailed biochemical and functional characterization would be required to draw the attention of this audience-
Scientifically, I have experience in the DNA topology and topoisomerases field, 3D genome organization and gene regulation. I have no experience in Gliomas or any other clinical aspect of cancer, so it is difficult for me to properly establish the potential impact of the newly discovered mutations. Technically I have no capacity to critically evaluate the aspects related to the targeted exome sequencing and the suitability of the analysis performed for mutation identification.
Referee Cross-commenting
I fully agree with the comments of the other reviewer, which are perfectly aligned with my own regarding the preliminary nature of the conclusions about the biochemical and functional characterization of the TOP2A mutations.
-
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Referee #1
Evidence, reproducibility and clarity
Summary:
Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate). Please place your comments about significance in section 2. In this paper the authors used a targeted approach to identify rare mutations in a cohort of glioma patients. Using this approach they identified a recurrent mutation in the TOP2A gene encoding for Topoisomerase 2A, and suggest that this mutation creates a more effective protein, binding DNA strongly and maybe more enzymatically active. RNAseq analysis of TOP2Awt and TOP2Amut tumor samples suggest different transcription patterns and points to possible splicing defects. The most recurrent variant (E9448Q) is described in depth and some experimental information shows this variant might be a gain-of-function mutation.
Major comments:
• Are the key conclusions convincing? The validation of both the methodology and the presence of never described TOP2A variations in HGG is done quite successfully. Interesting evidence about relevance of the most frequent mutation is provided. However, besides having computational and biochemistry assays performed, lack of details about in vitro experiment statistics (no p-values are provided in figures 4 and 5, neither sample size, repetitions) weakens the conclusions claimed by the authors about the properties of the mutated topoisomerase.
• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? Claims about E948Q variant function should be revised. Data is not presented in a convincing way, plus there is ambiguous language used from the results ("We conclude that the E9448Q TOP2A protein is functional, and MIGHT have a higher activity than the WT protein") to the rest of the paper where they strongly support the claims about the TOP2A activity.
• 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. In line with the presented data in the paper, additional experiments that show catalytic changes of the E9448Q variation must be added. It is shown that there are differences in the DNA binding capacity by EMSA compared to the WT form, however, the DNA supercoil relaxation activities is not that different, at least the way the results are presented. The authors suggest that TOP2A mutation is a driver mutation but no validation in vitro of this claim is shown. Can this mutation alone or in combination with e.g. tumor suppressors transform normal cells to cancer cells? Do cell lines expressing this mutation (compared to parental TOP2A wt expressing cells) display increased transcription? Increased invasion?
• 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. If the authors can complement the already presented in vitro experiments with additional ones supporting their hypothesis, this should be feasible. The authors can use patient derived glioma cells or glioma cell lines manipulated to express either the parental TOP2A wt enzyme or the identified mutated form.
• Are the data and the methods presented in such a way that they can be reproduced? Yes, the authors provide a quite detailed explanation of the methods implemented to reach each one of the results they are presenting.
• Are the experiments adequately replicated and statistical analysis adequate? No, there is no information about the statistical analysis or number of replicates in any of the in vitro experiments performed. This information should be added to the manuscript.
Minor comments:
• Specific experimental issues that are easily addressable.
• Are prior studies referenced appropriately? Yes, authors clearly address the state of the art regarding previous NGS methodologies and let us know the advantages and novelty of their approach.
• Are the text and figures clear and accurate? There are some discrepancies between the strength of the language used in different sections of the paper to refer the conclusions they can infer from the results they are showing. While they are all valid, authors should revise it.
• Do you have suggestions that would help the authors improve the presentation of their data and conclusions? First of all, describe the statistical analysis used in every figure, include number of biological and technical replicates. I would also suggest to change the title or the scope of the discussion, there is too much focus on the TOP2A in the introduction, neglecting all the technical NGS work that actually lead to several new variants being described. This may be confusing when it collides with a conclusion that is heavily focused on the first half describing potential implications of at least another 3 proteins where genetic alterations were described. Given the fact there is not much experimental work that shows TOP2A mutations relevance in HGG or strong enough evidence of the variant's function I would suggest to change a bit the scope of the title.
Significance
• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. The authors describe a methodology that proved to be sensitive and specific enough in order to allow them to detect rare genetic alterations in patient glioma samples. This information could be valuable to describe new driver mutations or infer in genetic pathway alterations that could be potential therapeutic targets. As the authors state at the beginning of the paper, given the poor therapeutical approaches existing for HGG currently, information of this kind could still be highly useful and provide a better outcome to a specific cohort of patients.
On a personal note, I think there is too much speculation about how TOP2A mutations could be interesting from a biological point of view (authors referred to evidence about implications of this mutation in other forms of cancer) but since no experimental validation is provided in glioma cells, it is difficult to conclude that this enzyme gain-of-function mutation could have a relevant role in HGG and thus make these variants a potential therapeutic target. There are no experiments conducted in glioma cells that express TOP2A variants, it would be interesting to see if it has an effect in the migratory/invasive phenotype like described in other cancer types or like it is suggested by analysis of the genetic pathways activated in the HGG patients samples harboring TOP2A mutation. In addition, there is no evidence of the TOP2A mutations possible role as a driver mutation, which is an interesting aspect that could be further explored from both a computational and an experimental approach.
• Place the work in the context of the existing literature (provide references, where appropriate). The quality of the paper is high and in line with other studies in the literature that perform genome and transcriptome analysis of tumor samples. It is only the experimental validation that is lacking data supporting the "in silico" findings.
• State what audience might be interested in and influenced by the reported findings. Computational biologists are the right audience to target this paper. If additional experimental work further validating their initial bioinformatic findings is added to the manuscript then probably a wider population could be targeted.
• 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. Brain tumors, immunotherapy, cancer stem cells, tumor microenvironment, tumor heterogeneity. I do not have sufficient expertise to evaluate the bioinformatic analysis and software/programs used to analyze the NGS data.
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Reply to the reviewers
We are grateful for the constructive and highly supportive reviews provided by our Reviewers. We especially appreciate the efforts they have made to provide suggestions on how to make our revised manuscript even more robust. We have incorporated many of these suggestions into the revised manuscript that will post to Biorxiv and will be submitted to an affiliate journal. We have provided point-by-point responses to each Reviewer below each item (starting with Response: …), along with any changes made in response to that comment/suggestion (starting with In our revised manuscript, …).
Finally, we agree with all Reviewers that this work should be of broad interest to the molecular biology, cell biology, and parasitology communities. Our discovery that Plasmodium and two related genera have taken the unorthodox approach of duplicating their NOT1 protein, and that Plasmodium has dedicated it for its unique transmission strategy, is a fascinating adaptation of the use of this core eukaryotic complex. We believe that those that focus on diverse aspects of RNA biology, including RNA preservation/decay, the maternal to zygotic transition, translational repression, and beyond will find this work to be of interest and relevant to their own research questions.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
The manuscript „The Plasmodium NOT1-G paralogue acts as an essential nexus for sexual stage maturation and parasite transmission" investigates the two forms of NOT1 in rodent malaria parasites. The authors found out that the original NOT1 is crucial for gametocyte induction as well as transmission to the mosquito, they therefore renamed it NOT1-G. The paralogous proteins, on the other hand, appears to be crucial for intraerythrocytic growth, since it cannot be knocked out. The authors then investigated NOT1-G in more detail, using standard phenotyping assays. They found a slightly increased gametocytemia and a minor effect on transmission to the mosquito.
Response: In our submitted manuscript, we do focus on PyNOT1-G because of the exciting role it has for both sexes of gametocytes, which results in a complete defect in transmission to mosquitoes. Our investigations of what domains of PyNOT1-G focused on the most likely suspect: the putative tristetraprolin-binding domain (TTPbd). It was through deletion of this domain that we observed only a minor defect in the prevalence of infection of mosquitoes, indicating that the portion of PyNOT1-G that is required for transmission lies elsewhere (in part or in total). It is also important to correct Reviewer 1’s statement regarding the other (perhaps canonical) PyNOT1. To our surprise, PyNOT1 could be deleted, but resulted in a parasite that has an extreme fitness cost and a very slow growth phenotype. This is in stark contrast to other eukaryotes, where NOT1 is essential.
Reviewer #1 (Significance (Required)):
If the authors are able to provide convincing data that NOT1-G is indeed important for gametocyte induction and transmission to the mosquito, then the report would be of high significance for the malaria and molecular cell biology fields.
Response**: We have in fact shown this and more in the originally submitted manuscript, and thus we are grateful that Reviewer 1 considers this work to be of high significance in a broad readership (molecular and cell biology, parasitology). In our revised manuscript, we have added text throughout to make these results even more apparent and clear for the reader.
My expertise: molecular cell biology of gametocytes, translational regulation, parasite transmission
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
**Summary**
The manuscript by Hart et al. builds upon a fascinating finding presented in a previous manuscript by the same authors, in which they show that CCR4 seems to be able to associate with two members of the NOT1 family. In this work, the authors first re-annotate the two NOT1 paralogs in Plasmodium yoelii and then perform an in depth characterization of the role of NOT1-G during gametocytogenesis and early mosquito development. Using gene knockout and different genetic crosses, the authors show that NOT1-G is essential for male gametocyte development and leads to an arrest of development in zygotes arising from female gametocytes. Using RNA-seq the authors show that NOT1-G leads to lower transcript abundances, leading to the hypothesis that NOT1-G might be involved in preserving mRNAs in a larger RNA-binding complex. Lastly, the authors characterize a NOT1-G defining TPP domain and find that it is not essential for either male/female phenotype observed for the whole gene KO.
Response**: We appreciate the concise and accurate summary of these findings.
**Major comments:**
Are the key conclusions convincing?
The phenotypic characterization of NOT1-G during gametocytogenesis / early mosquito development is nicely presented and the experiments are well performed. Because a duplication of NOT1 with possibly opposing roles of the paralogs is a very unique feature with broad implication on RNA metabolism, it would have been great to see two select experiments on the molecular level adding evidence that 1) NOT1/NOT1-G are mutually exclusive in a complex with CCR4/CAF1 and 2) NOT1-G acts post-transcriptionally in an antagonistic way to NOT1 (i.e. as a mRNA 'stabilizer' as proposed by the authors).
Response**: We agree that inclusion of those two aspects would make for a more complete story about these two NOT1 paralogues.
First, we also think that it is highly likely that NOT1 and NOT1-G are mutually exclusive, as in other eukaryotes NOT1 acts as a scaffold protein upon which effector proteins bind and bridging interactions are made. In our original manuscript, we did not include a mention of our previous attempts to address this question through colocalization and proteomic approaches, as they were largely unsuccessful. Specifically, we generated rabbit polyclonal antisera to PyNOT1-G’s tristetraprolin-binding domain but it did not pass our rigorous quality control (e.g. too much staining persisted in pynot1-g- parasites). Using both asexual and sexual blood stage parasites, we also attempted immunoprecipitation (with and without chemical crosslinking) and proximal labeling approaches via BioID and TurboID but all approaches did not produce rigorous results and thus we did not report them in our original manuscript. However, this question of whether the two NOT1 paralogues were mutually exclusive in complexes was also taken up by the Bozdech Laboratory in their 2020 preprint (Liu et al.) where they were able to capture the P. falciparum NOT1-G and NOT1 proteins (called Not1.1 and Not1.2 in that work). While their proteomic evidence showed that they could capture these bait proteins and that the NOT1 paralogues were not in the same complex, these results should be taken with a grain of salt: all mass spectrometry-based proteomic approaches are limited in that an absence of evidence does not mean that the protein is not present/interacting. Moreover, these efforts only identified a few other proteins that were already known to interact with the CAF1/CCR4/NOT complex, but even so, they did not use statistically rigorous methods in an attempt to quantify these results. In our revised our manuscript, we have included additional text to describe our unsuccessful efforts to do these capture proteomics experiments, and we have expanded our discussion of the Liu et al findings that provide some evidence in support of a mutually exclusive complex.
Second, we also hypothesize that PyNOT1-G acts post-transcriptionally to affect mRNA abundance and translation. However, it is important to emphasize that NOT1 proteins typically act as scaffolds, with the recruited effector proteins acting to hasten the degradation and/or to preserve associated transcripts. We believe that studying these effector proteins is the next important effort to undertake. In fact, we hypothesized that these antagonistic effector proteins would be analogous to TTP and ELAV/HuR-family proteins as are found in other eukaryotes, and that the critical interaction with PyNOT1-G would be via its putative TTP-binding domain. It was for that reason that we interrogated the TTP-binding domain itself, and were surprised that its deletion did not phenocopy the complete gene deletion. Ongoing work will be focused on identifying these antagonistic effector proteins that likely are expressed in a stage-enriched manner, and to define how they interact with PyNOT1-G in order to direct specific mRNAs to their fates. Additionally, it would be very important and exciting to directly test if PyNOT1 and PyNOT1-G are functionally opposed. However, this would be exceptionally challenging to study from a technical standpoint. While we were able to delete the pynot1 gene after many repeated attempts, these parasites are very sickly and grow very slowly. Because of this, we believe that assessing direct versus indirect effects of PyNOT1 in these cells would not be feasible or robust. Given this, comparing functions between PyNOT1 and PyNOT1-G could not be done in a conclusive manner.** In our revised manuscript, we have expanded our descriptions of the mechanisms by which we believe PyNOT1-G and its complex affects mRNA fates. In particular, we have expanded our Discussion section to incorporate the results that indicate that the TTP-binding domain is not required for the essential functions of PyNOT1-G.
Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?
The authors describe the role of NOT1-G as 'preserving' mRNA. The lower abundance of many transcripts in the NOT1-G knockout suggest this, but experimental proof is not provided (see suggestions below). Maybe rephrase to 'putatively preserved/stabilized' or 'has a potentially stabilizing function'. The same is true for the mutually exclusive association of the two paralogs with CCR4/CAF1. The authors refer to a protein co-IP of CCR4 showing that CCR4 can interact with both NOT1 and NOT1-G, but a reciprocal experiment is lacking.
Response**: In our first publication on the deadenylase members of this complex, we also saw a similar effect on specific mRNAs when pyccr4-1 was deleted: the abundance of specific mRNAs went up in pyccr4-1- parasites. In that work and here in this manuscript, we have carefully decided to apply the word “preserved” to the fate of these mRNAs as it describes in a general way what is happening. In order to robustly state that mRNAs are stabilized by PyNOT1-G (directly or indirectly) would require additional experiments designed to test this (more description on this is provided on a response below). Second, as described above, we agree that doing a reciprocal IP for mass spectrometry-based proteomics would be ideal, we attempted four different approaches to do this to no avail. However, the composite proteomics data that is already available in the literature and via the Liu et al. preprint from the Bozdech Lab all indicate that these interactions occur, and perhaps that NOT1 and NOT1-G are mutually exclusive as expected. In our revised manuscript, we have provided further explanation in the Discussion for our use of the descriptor “preserve” instead of “stabilize”, and as noted above, and we have expanded our Discussion to more comprehensively define the interaction network depicted in Figure 7.
In both cases, the conclusions of the authors are very likely (e.g. downregulation of many genes as seen by RNA-seq), but the final experimental evidence is not provided and a network such as in Figure 7 is not fully supported. If the authors would like to maintain these statements, then they should be rephrased and made clear or the additional experimental evidence suggested below is necessary.
Response**: We hold that the published proteomic datasets do support such a network, with further support offered from the preliminary proteomic evidence from the Liu et al preprint. Therefore, we have not modified our manuscript beyond the additional text now provided in the Discussion as noted above.
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 essential claim that NOT1-G is important for gametocytogenesis and early mosquito development is well presented and fully supported by the experiments. As for the role of NOT1-G in 'preserving' mRNA, an mRNA half-life experiment would be necessary (or the text should be adjusted as mentioned above). In a short-term in vitro culture, pynot1-g- and WT parasites could be treated with ActD and abundances of select transcripts are measured by RT-qPCR.
Response**: We appreciate that Reviewer 2 considers the rigor of our experiments to be high. Regarding the use of the term “preserve” vs “stabilize”, we agree that to shift from our more general descriptor (preserve) to one that has specific connotations (stabilize) would require additional experimentation. To correctly and most robustly make the claim of stabilization would require work on par with that done by Painter et al. (PMID: 29985403) that uses a thiol-containing nucleotide (4-TU) along with a yeast-derived fusion enzyme (yFCU) to convert it for use by Plasmodium. Previously we have shown that an associated deadenylase (PyCCR4-1) also acted to preserve mRNAs, and moreover that deletion of its gene resulted in no discernable effect upon the poly(A) tail or 3’ UTR of an mRNA that is bound by this complex (p28).
While understanding mRNA stability is an exciting area of study, this 4-TU labeling experiment alone warranted a standalone, high impact publication for Painter et al. As this has not been adapted for any rodent-infectious Plasmodium species to date, and as adaptation of this labeling approach took several years for Dr. Painter while in the Llinas Laboratory (personal communication), we believe this work is beyond the scope of this study. Moreover, the additional information that it would provide to understand NOT1-g functions (preserve vs stabilize) would be incremental beyond the major storyline presented in this manuscript. In our revised manuscript, we have added text to ensure that our choice of “preserve” is well defined and explained.
To support the idea that NOT-1 and NOT1-G associate in a mutually exclusive way or to just show that they act in distinct complexes despite their similar expression patterns, an IFA with a double stained NOT1/NOT-1G cell line could be performed. Alternatively, the authors could perform a protein co-IP using the already existing NOT1/NOT1-G-GFP cell line and show that the proteins don't interact with each other or even have certain distinct interaction partners.
Response**: We agree, and these studies were attempted but were unsuccessful (described in our responses above). In our revised manuscript, we have included this information as noted above.
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.
All necessary cell lines for a NOT1/NOT1-G co-IP and the ActD experiment are already present. The authors already present a ring to schizont in vitro culture (for ActD) and also have substantial experience in protein co-IP and proteomics.
I am not sure about the cost for a proteomics experiment at the author's institute and I don't want to make a guess on time investment given the still on-going COVID situation.
Response**: We agree that these experiments would be interesting, and would be costly to do at a transcriptome-wide scale and would require substantial time to conduct. We believe that the 4-TU approach noted above is the most rigorous, but is well beyond the scope of this study as it has not yet been adapted to rodent-infectious malaria parasites. As noted above, we have attempted four different proteomics approaches to provide reciprocal evidence for the complex composition which were unsuccessful. In our revised manuscript, we have added text to ensure that our choice of “preserve” is well defined and explained, and have noted the unsuccessful reciprocal proteomics approaches.
Are the data and the methods presented in such a way that they can be reproduced?
The MM section is well structured and presented and the supplemental material includes all data.
Response**: Thank you. We want to ensure that our work is clearly described and can be reproduced with the information reported.
Are the experiments adequately replicated and statistical analysis adequate?
There is hardly any test of significance presented in the main text of the manuscript (e.g. Figure 3B and 4A). Please show the individual data points for these graphs and make sure the n= and the statistical test is described in the figure legend. If you use the term significant in the text, then just add the p-value behind it. This is also true for the RNA-seq data: Genes are sorted by fold-changes, leaving it unclear if these changes are significant. These data are however presented in Table S1 and could be incorporated in the main text.
Response**: We agree. In our revised manuscript, we have incorporated additional details about the statistical tests used, p-values for noteworthy comparisons, and have included more panels for our comparative RNA-seq datasets (heatmap, PCA, MA plots). We have also made adjustments to our plots to make individual data points more readily observed, especially when error bars may block them (e.g. Figure 3B). And as in the original submission, all of the pertinent values, including fold changes, statistics and more are provided in our comprehensive supplementary files. We have structured the Supplementary Tables to flow from one tab to the next with the filtering/threshold applied noted both in the tab name and in the README tab that is found first among the tabs.
**Minor comments:**
Specific experimental issues that are easily addressable.
One idea that is also not discussed but could be added is for example that NOT1-G itself doesn't even have a stabilizing effect itself, but act as a decoy for other components of the CCR4/Caf1 complex, keeping them from associating with NOT1. In the NOT1-G knockout, the decrease in RNA abundance might then be just a result of an 'overactivity' of CCR4/Caf1/NOT1.
Response**: This hypothesis proposed by Reviewer 2, that PyNOT1-G is acting as a decoy or a binding partner sponge, is certainly feasible. For this scenario to be effective, PyNOT1-G would need to be in excess of PyNOT1 and/or would need to be able to bind to the critical effector protein(s) better than does PyNOT1. However, our microscopy data, along with the transcriptomic data presented here and previously published proteomic data would indicate that these two gene products are in approximately balanced proportions and are similarly localized. This does not exclude the possibility that PyNOT1-G could act as a sponge for relevant binding partners. In our revised manuscript, we have raised this possibility as an alternate explanation for the phenotype in the Discussion section.
Are prior studies referenced appropriately?
Throughout the manuscript, the authors should make clear what results come from which organism. Just as an example, the genome wide KO screens were performed in P. berghei and P. falciparum, CCR4/CAF1 experiments were performed in P. yoelii, whereas the original DDX6 work was done in P. berghei.
Response**: We agree. In our revised manuscript, we have added additional text to further clarify what data comes from which Plasmodium species.
Are the text and figures clear and accurate?
The Introduction is a bit long and partially turns into a minireview of eukaryotic RNA degradation. In the main text on page 13, the authors introduce a model for proteins involved in translational repression. This in not fully accurate, since for many of the proteins in this network, an effect on translation has actually not been shown. This includes NOT1-G characterized in the present work that most likely has an effect on mRNA stability, but for which a role in regulating translation is not presented.
Response**: We believe the length and content of this Introduction is appropriate to provide the context that some readers outside of the parasitology field will need to appreciate these findings. Regarding designations for these proteins as being related to translational repression, we think that the ample proteomic evidence tying them to translationally repressive complexes warrants this. In our revised manuscript, we have made it more clear that these proteins themselves have not been directly implicated in translational repression.
Do you have suggestions that would help the authors improve the presentation of their data and conclusions?
Overall the RNA-seq is underrepresented and Figure 5 could easily be expanded by adding several panels that would help the future reader getting a better idea of the data:
- Summary graphs such as PCA/MDS plots of the different replicates and MA-plots (all of which can be easily generated in DESeq2)
- Heatmaps comparing the expression patterns of pynot1-g-, pbdozi-, pbcith-, pyalba4- highlighting some key gametocyte genes mentioned in the text
Alternatively to 2., a simple Venn Diagram would already be very informative
An informative representation might also be to sort the differentially expressed genes as predominant male and/or female. The P. berghei data by Yeoh et al (PMID: 28923023) could be a starting point.
Response**: We agree. In our revised manuscript, we have expanded Figure 5 to include additional plots that speak the rigor of these datasets. Specifically, we have added a comprehensive heatmap and PCA plots, as well as MA plots as recommended. We have chosen not to include a Venn diagram for the overlap of affected mRNAs across these transgenic parasite lines, as we hold that this information is best provided in the text (high level observations) and the Supplement (details).
Reviewer #2 (Significance (Required)):
**Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.**
Technically this manuscript builds on standard methods of the field that are well executed. There is no direct clinical advancement, although one might argue that a unique adaptation of the parasite could always be a novel therapeutic target. Conceptually this is great advancement for the parasitology field as it is, providing additional evidence for the importance of post-transcriptional regulation for parasite transmission. With the two experiments suggested above and the additional evidence gained from it, this manuscript could also gain great interest to readers outside the field by clearly showing how alternative ways to regulate RNA stability evolved.
Response**: We are grateful for your careful review of our work and for the recommendations that you provided. We have incorporated many of them into the revised manuscript to make it even more rigorous and comprehensive. We also appreciate hearing that this work would be of great interest to a broader community. We feel that this is already the case, as the duplication of NOT1 and the dedication of one paralogue to an essential function is exciting and novel among eukaryotes.
**Place the work in the context of the existing literature (provide references, where appropriate)**
The work builds on the early reports of the particular RNA metabolism in gametocytes performed in the groups of Andy Waters. Since then, the authors themselves have published a great set of manuscripts extending our knowledge of the proteins involved in gametocytogenesis and nicely place the current work into this framework.
Response**: We appreciate this positive feedback. This is a fascinating topic to study.
**State what audience might be interested in and influenced by the reported findings.**
The manuscript as it stands is particularly interesting for the parasitology and potentially the evolutionary biology field. For a broader readership for example in the RNA field, the possibly antagonistic roles and mutually exclusive association with CAF1/CCR4 are likely most interesting.
Response**: We agree that this should be interesting to readers beyond our own field, as the duplication and specialization of NOT1, and the finding that the “canonical” PyNOT1 can be deleted, are both of general interest to how eukaryotes have adapted and deployed a highly conserved and essential RNA metabolic complex.
**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.**
**Expertise:**
RNA biology, Plasmodium falciparum, Bioinformatics
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
In this manuscript, the authors investigate the requirement of two possible Not1 paralogs for the development of asexual blood stages and for the sexual transmission stages of Plasmodium yoelii. While Not1 is critical for asexual blood stages, its putative paralog, Not1G is important for the development of sexual transmission stages. In the absence of Not1G, male gametes are not formed while female gametes are formed and can be fertilised by wt male gametes. However, the resulting zygote cannot develop further into ookinete. The in vitro genetic cross assay to show this is elegant! A transcriptomic analysis further indicates that the transcriptomes of Not1G deficient parasites are significantly different from their WT counterpart.
Response**: We are thrilled that you found our evidence and approaches to be rigorous and compelling. Thank you.
**Major comments:**
The discussion section is very nice and the authors describe well what is speculative and should be further confirmed by additional experiments. However, I did find this was not the case in the results section where the authors are proposing conclusions that are not supported by the results. I think the reading of this manuscript would be much more enjoyable if the authors only describe the results shown and move all the discussions to the dedicated section. Below are some examples. The data presented in this manuscript is not showing a nexus, this is a suggestion based on the results of other articles, the word should thus be removed from the title (and kept for a future review!). The last two sentences of the localisation section should be moved to the discussion because they do refer to results not shown in this manuscript. The last sentence of the second paragraph of the zygote development section should also be moved to the discussion. For the transcriptomic analysis there is also no formal comparison with transcriptomes of other previously analysed mutants: the results of the comparisons should either be shown or not discussed in the result section. Finally, the discussions mentioning interactors of the complex should be removed from the result section and moved to the discussion unless the results are formally analysed.
Response**: We again thank you for the complement. In our original manuscript, we opted to provide some limited interpretations and context within the Results section in order to help guide readers along our train-of-thought and line-of-experimentation. While a more traditional split of keeping essentially all discussion and interpretation for the Discussion is a tried-and-true approach, we prefer this more narrative method and have opted to keep these short sections in the Results section.
I would strongly suggest the author the better present and describe their transcriptomic results. There is only one volcano plot indicating the overall defect in mixed gametocytes in the main figure. Apart from this, the results are only described in the main text or in supplementary tables. It is therefore difficult to understand the subtilities of the analysis. For example, the authors frequently mention dysregulated genes, but without specifying whether it is up or down-regulated in the mutant. To address this issue, I would suggest the authors to better describe their results in the figures. They could show the GO term enrichment analysis they mention and show how they assign GO term or transcripts to male and female parasites. It would also be nice to discuss some of the results a bit more in details. For example, it is not surprising to see a reduction in transcripts that are under the control of AP2-O in retort-arrested ookinetes as the parasite do not reach this stage. It is thus highly speculative to specifically link this observation with ALBA4 without further detailed analysis. On the other hand, it is more surprising to see a decrease in ap2g transcripts, while the authors observe an increased gametocytaemia. Could the authors comment this observation? It may also be nice to better present the comparison between gametocytes and schizonts to possibly speculate on the early requirement of Not1G in committed schizonts.
Response**: We (and Reviewer 2) agree. In our revised manuscript, we have expanded Figure 5 to include additional plots that speak the rigor of these datasets. Specifically, we have added a heatmap, and PCA and MA plots as recommended. We have chosen not to include a Venn diagrams for the overlap of affected mRNAs across these transgenic parasite lines for the reasons stated above in our response to Reviewer 2. Similarly, we have opted to keep the specifics of the GO Term analyses in the Supplement as we believe these should always be taken with a grain of salt (especially high level GO Terms, as many choose to report). Finally, we have expanded our discussion on our observation that pyapiap2-g transcript levels are lower in the pynot1-g- line, despite seeing a slight increase in gametocytemia.
The conclusion regarding the similar localisation of Not1 and Not1G with other members of the CAF1/CCR4/NOT complex is not really convincing for two reasons. First, there is not colocalization shown and, second, the distribution is not very peculiar so it is difficult to draw any conclusion with this level of resolution. The presence of alpha-tubulin in the nucleus of male gametocytes is also very surprising as it is rather nucleus-excluded in both P. falciparum and P. berghei, could the authors comment this peculiar localisation?
Response**: We agree and disagree here. First, we agree that no colocalization data is presented here to place NOT1-G within the limit of resolution of fluorescence microscopy. What we can (and do) state is that these proteins are all localized to cytosolic puncta, which matches what is observed for essentially all other studied eukaryotes. In further support of this, our published, quantitative proteomic data indicates that the bioinformatically predictable members of the CAF1/CCR4/NOT complex do associate as anticipated. In the same vein, the micrographs presented were not captured by confocal microscopy, and thus the apparent localization of alpha tubulin “in” the nucleus is most likely attributed to being above and/or below the nucleus. Taken together, we do feel that the combined evidence is convincing. As we have already made all of these points in the original manuscript, we have not adjusted the revised manuscript further.
One of my major frustration when reading this manuscript was that the authors are not trying to discriminate between an early role of Not1G during gametocytogenesis or later in gametogenesis. The fact that the transcriptomes of gametocytes and schizonts seem to show similarities suggests that the phenotype observed during both male gametogenesis or ookinete development are probably linked to early knock-on defects during gametocytogenesis. Could the authors test whether male gametocytes replicate DNA or female activate translation? These are of course non-essential experiments as the authors are careful with their conclusions and mention possible defects during both gametocytogenesis or gametogenesis. Addressing this question may however add significant insights into the requirement for Not1G.
Response**: We are sorry for the frustration. We wrote the manuscript so as to state what we feel we could robustly say, and where we are drawn to speculate, we made that speculation clear. As Reviewer 3 notes, we have not attempted to discriminate between functions that PyNOT1-G may be playing in different stages or substages of development because we do not believe the experiments allow that discrimination. While we could investigate finer and finer aspects of possible defects in both male and female gametocyte development, the most impactful take home messages remain the same. We continue to address questions related to translational repression and its release, and anticipate that PyNOT1-G will play a substantial and essential role in this. As Reviewer 3 noted, we have already discussed these possibilities in the original manuscript, and thus have not added anything further about this in our revised manuscript.
**Minor comments:**
Please use page and line numbering for your next submissions! Please describe what "bioinformatics" was used. I would show the nice localisation in oocyst and sporozoite in the main section. The conclusions drawn from the genetic cross seem to come from a single biological replicate, if this is the case please indicate it clearly.
Response**: We apologize for these oversights. In our revised manuscript, we have provided page and line numbering, have expanded on what bioinformatic processes were done in the manuscript, and have made it more clear that the genetic crosses come from multiple biological replicates (biological triplicate for the transmission-based genetic cross, biological duplicate for the in vitro culture genetic cross). However, we have opted to retain the oocyst and sporozoite IFA data in the Supplement, as the rest of the story is focused on blood stage and early mosquito stage.
Reviewer #3 (Significance (Required)):
This manuscript highlights the requirement of a Not1 paralog in the transmission stages of a Plasmodium parasite. More specifically it describes a new player in the control of RNA biology during this process where our knowledge is scarce. It will be a valuable manuscript for molecular parasitologists interested in transmission or RNA biology.
Response**: We agree and are grateful that our colleagues find this study to be a valuable addition in our efforts to understand how malaria parasites have adapted classic eukaryotic mechanisms to suit their purposes.
Our expertise is largely in molecular and cellular parasitology.
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Referee #3
Evidence, reproducibility and clarity
In this manuscript, the authors investigate the requirement of two possible Not1 paralogs for the development of asexual blood stages and for the sexual transmission stages of Plasmodium yoelii. While Not1 is critical for asexual blood stages, its putative paralog, Not1G is important for the development of sexual transmission stages. In the absence of Not1G, male gametes are not formed while female gametes are formed and can be fertilised by wt male gametes. However, the resulting zygote cannot develop further into ookinete. The in vitro genetic cross assay to show this is elegant! A transcriptomic analysis further indicates that the transcriptomes of Not1G deficient parasites are significantly different from their WT counterpart.
Major comments:
The discussion section is very nice and the authors describe well what is speculative and should be further confirmed by additional experiments. However, I did find this was not the case in the results section where the authors are proposing conclusions that are not supported by the results. I think the reading of this manuscript would be much more enjoyable if the authors only describe the results shown and move all the discussions to the dedicated section. Below are some examples. The data presented in this manuscript is not showing a nexus, this is a suggestion based on the results of other articles, the word should thus be removed from the title (and kept for a future review!). The last two sentences of the localisation section should be moved to the discussion because they do refer to results not shown in this manuscript. The last sentence of the second paragraph of the zygote development section should also be moved to the discussion. For the transcriptomic analysis there is also no formal comparison with transcriptomes of other previously analysed mutants: the results of the comparisons should either be shown or not discussed in the result section. Finally, the discussions mentioning interactors of the complex should be removed from the result section and moved to the discussion unless the results are formally analysed.
I would strongly suggest the author the better present and describe their transcriptomic results. There is only one volcano plot indicating the overall defect in mixed gametocytes in the main figure. Apart from this, the results are only described in the main text or in supplementary tables. It is therefore difficult to understand the subtilities of the analysis. For example, the authors frequently mention dysregulated genes, but without specifying whether it is up or down-regulated in the mutant. To address this issue, I would suggest the authors to better describe their results in the figures. They could show the GO term enrichment analysis they mention and show how they assign GO term or transcripts to male and female parasites. It would also be nice to discuss some of the results a bit more in details. For example, it is not surprising to see a reduction in transcripts that are under the control of AP2-O in retort-arrested ookinetes as the parasite do not reach this stage. It is thus highly speculative to specifically link this observation with ALBA4 without further detailed analysis. On the other hand, it is more surprising to see a decrease in ap2g transcripts, while the authors observe an increased gametocytaemia. Could the authors comment this observation? It may also be nice to better present the comparison between gametocytes and schizonts to possibly speculate on the early requirement of Not1G in committed schizonts.
The conclusion regarding the similar localisation of Not1 and Not1G with other members of the CAF1/CCR4/NOT complex is not really convincing for two reasons. First, there is not colocalization shown and, second, the distribution is not very peculiar so it is difficult to draw any conclusion with this level of resolution. The presence of alpha-tubulin in the nucleus of male gametocytes is also very surprising as it is rather nucleus-excluded in both P. falciparum and P. berghei, could the authors comment this peculiar localisation?
One of my major frustration when reading this manuscript was that the authors are not trying to discriminate between an early role of Not1G during gametocytogenesis or later in gametogenesis. The fact that the transcriptomes of gametocytes and schizonts seem to show similarities suggests that the phenotype observed during both male gametogenesis or ookinete development are probably linked to early knock-on defects during gametocytogenesis. Could the authors test whether male gametocytes replicate DNA or female activate translation? These are of course non-essential experiments as the authors are careful with their conclusions and mention possible defects during both gametocytogenesis or gametogenesis. Addressing this question may however add significant insights into the requirement for Not1G.
Minor comments:
Please use page and line numbering for your next submissions! Please describe what "bioinformatics" was used. I would show the nice localisation in oocyst and sporozoite in the main section. The conclusions drawn from the genetic cross seem to come from a single biological replicate, if this is the case please indicate it clearly.
Significance
This manuscript highlights the requirement of a Not1 paralog in the transmission stages of a Plasmodium parasite. More specifically it describes a new player in the control of RNA biology during this process where our knowledge is scarce. It will be a valuable manuscript for molecular parasitologists interested in transmission or RNA biology.
Our expertise is largely in molecular and cellular parasitology.
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Referee #2
Evidence, reproducibility and clarity
Summary
The manuscript by Hart et al. builds upon a fascinating finding presented in a previous manuscript by the same authors, in which they show that CCR4 seems to be able to associate with two members of the NOT1 family. In this work, the authors first re-annotate the two NOT1 paralogs in Plasmodium yoelii and then perform an in depth characterization of the role of NOT1-G during gametocytogenesis and early mosquito development. Using gene knockout and different genetic crosses, the authors show that NOT1-G is essential for male gametocyte development and leads to an arrest of development in zygotes arising from female gametocytes. Using RNA-seq the authors show that NOT1-G leads to lower transcript abundances, leading to the hypothesis that NOT1-G might be involved in preserving mRNAs in a larger RNA-binding complex. Lastly, the authors characterize a NOT1-G defining TPP domain and find that it is not essential for either male/female phenotype observed for the whole gene KO.
Major comments:
- Are the key conclusions convincing?
The phenotypic characterization of NOT1-G during gametocytogenesis / early mosquito development is nicely presented and the experiments are well performed. Because a duplication of NOT1 with possibly opposing roles of the paralogs is a very unique feature with broad implication on RNA metabolism, it would have been great to see two select experiments on the molecular level adding evidence that 1) NOT1/NOT1-G are mutually exclusive in a complex with CCR4/CAF1 and 2) NOT1-G acts post-transcriptionally in an antagonistic way to NOT1 (i.e. as a mRNA 'stabilizer' as proposed by the authors).
- Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?
The authors describe the role of NOT1-G as 'preserving' mRNA. The lower abundance of many transcripts in the NOT1-G knockout suggest this, but experimental proof is not provided (see suggestions below). Maybe rephrase to 'putatively preserved/stabilized' or 'has a potentially stabilizing function'. The same is true for the mutually exclusive association of the two paralogs with CCR4/CAF1. The authors refer to a protein co-IP of CCR4 showing that CCR4 can interact with both NOT1 and NOT1-G, but a reciprocal experiment is lacking.
In both cases, the conclusions of the authors are very likely (e.g. downregulation of many genes as seen by RNA-seq), but the final experimental evidence is not provided and a network such as in Figure 7 is not fully supported. If the authors would like to maintain these statements, then they should be rephrased and made clear or the additional experimental evidence suggested below is necessary.
- 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 essential claim that NOT1-G is important for gametocytogenesis and early mosquito development is well presented and fully supported by the experiments. As for the role of NOT1-G in 'preserving' mRNA, an mRNA half-life experiment would be necessary (or the text should be adjusted as mentioned above). In a short-term in vitro culture, pynot1-g- and WT parasites could be treated with ActD and abundances of select transcripts are measured by RT-qPCR.
To support the idea that NOT-1 and NOT1-G associate in a mutually exclusive way or to just show that they act in distinct complexes despite their similar expression patterns, an IFA with a double stained NOT1/NOT-1G cell line could be performed. Alternatively, the authors could perform a protein co-IP using the already existing NOT1/NOT1-G-GFP cell line and show that the proteins don't interact with each other or even have certain distinct interaction partners.
- 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.
All necessary cell lines for a NOT1/NOT1-G co-IP and the ActD experiment are already present. The authors already present a ring to schizont in vitro culture (for ActD) and also have substantial experience in protein co-IP and proteomics.
I am not sure about the cost for a proteomics experiment at the author's institute and I don't want to make a guess on time investment given the still on-going COVID situation.
- Are the data and the methods presented in such a way that they can be reproduced?
The MM section is well structured and presented and the supplemental material includes all data.
- Are the experiments adequately replicated and statistical analysis adequate?
There is hardly any test of significance presented in the main text of the manuscript (e.g. Figure 3B and 4A). Please show the individual data points for these graphs and make sure the n= and the statistical test is described in the figure legend. If you use the term significant in the text, then just add the p-value behind it. This is also true for the RNA-seq data: Genes are sorted by fold-changes, leaving it unclear if these changes are significant. These data are however presented in Table S1 and could be incorporated in the main text.
Minor comments:
- Specific experimental issues that are easily addressable.
One idea that is also not discussed but could be added is for example that NOT1-G itself doesn't even have a stabilizing effect itself, but act as a decoy for other components of the CCR4/Caf1 complex, keeping them from associating with NOT1. In the NOT1-G knockout, the decrease in RNA abundance might then be just a result of an 'overactivity' of CCR4/Caf1/NOT1.
- Are prior studies referenced appropriately?
Throughout the manuscript, the authors should make clear what results come from which organism. Just as an example, the genome wide KO screens were performed in P. berghei and P. falciparum, CCR4/CAF1 experiments were performed in P. yoelii, whereas the original DDX6 work was done in P. berghei.
- Are the text and figures clear and accurate?
The Introduction is a bit long and partially turns into a minireview of eukaryotic RNA degradation. In the main text on page 13, the authors introduce a model for proteins involved in translational repression. This in not fully accurate, since for many of the proteins in this network, an effect on translation has actually not been shown. This includes NOT1-G characterized in the present work that most likely has an effect on mRNA stability, but for which a role in regulating translation is not presented.
- Do you have suggestions that would help the authors improve the presentation of their data and conclusions?
Overall the RNA-seq is underrepresented and Figure 5 could easily be expanded by adding several panels that would help the future reader getting a better idea of the data:
- Summary graphs such as PCA/MDS plots of the different replicates and MA-plots (all of which can be easily generated in DESeq2)
- Heatmaps comparing the expression patterns of pynot1-g-, pbdozi-, pbcith-, pyalba4- highlighting some key gametocyte genes mentioned in the text
- Alternatively to 2., a simple Venn Diagram would already be very informative
An informative representation might also be to sort the differentially expressed genes as predominant male and/or female. The P. berghei data by Yeoh et al (PMID: 28923023) could be a starting point.
Significance
Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.
Technically this manuscript builds on standard methods of the field that are well executed. There is no direct clinical advancement, although one might argue that a unique adaptation of the parasite could always be a novel therapeutic target. Conceptually this is great advancement for the parasitology field as it is, providing additional evidence for the importance of post-transcriptional regulation for parasite transmission. With the two experiments suggested above and the additional evidence gained from it, this manuscript could also gain great interest to readers outside the field by clearly showing how alternative ways to regulate RNA stability evolved.
Place the work in the context of the existing literature (provide references, where appropriate)
The work builds on the early reports of the particular RNA metabolism in gametocytes performed in the groups of Andy Waters. Since then, the authors themselves have published a great set of manuscripts extending our knowledge of the proteins involved in gametocytogenesis and nicely place the current work into this framework.
State what audience might be interested in and influenced by the reported findings.
The manuscript as it stands is particularly interesting for the parasitology and potentially the evolutionary biology field. For a broader readership for example in the RNA field, the possibly antagonistic roles and mutually exclusive association with CAF1/CCR4 are likely most interesting.
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.
Expertise:
RNA biology, Plasmodium falciparum, Bioinformatics
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Referee #1
Evidence, reproducibility and clarity
The manuscript „The Plasmodium NOT1-G paralogue acts as an essential nexus for sexual stage maturation and parasite transmission" investigates the two forms of NOT1 in rodent malaria parasites. The authors found out that the original NOT1 is crucial for gametocyte induction as well as transmission to the mosquito, they therefore renamed it NOT1-G. The paralogous proteins, on the other hand, appears to be crucial for intraerythrocytic growth, since it cannot be knocked out. The authors then investigated NOT1-G in more detail, using standard phenotyping assays. They found a slightly increased gametocytemia and a minor effect on transmission to the mosquito.
Significance
If the authors are able to provide convincing data that NOT1-G is indeed important for gametocyte induction and transmission to the mosquito, then the report would be of high significance for the malaria and molecular cell biology fields.
My expertise: molecular cell biology of gametocytes, translational regulation, parasite transmission
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Reply to the reviewers
We thank all four reviewers for their positive and constructive comments! We have carefully considered these comments and provided a point-by-point response below.
Reviewer #1 (Evidence, reproducibility and clarity):
This paper explores an interesting problem of SHP1/SHP2 preferences of inhibitory immunoreceptors. The author are quick to point out that many of their individual data points confirm published results at some level, but the power of the paper is in the parallel analysis of both PD1, which is strongly biased towards SHP2 and BTLA, which is biased towards SHP1. This gives them the opportunity to test the predictions of descriptive experiment by making simple mutated receptors with swapped ITIM or ITSM domains.
The work is very well done and generally the authors are quite careful and precise about the language used to describe results, in general.
The results are quite striking in that the find plenty of evidence for transient interaction of SHP1 with PD1 based on the biophysical measurements, but don't detect the interactions in pull down or in "in cell" microcluster recruitment experiments. In describing the pull-downs they discuss the issue of dissociation during washing potentially missing interactions that are taking place. I would prefer that the pull down is fine evidence for binding, but lack of pull down is not evidence for lack of binding. They should double check that this language is consistent. Also, unless something has changed in the microcluster binding experiments, this in situ recruitment of SHP2 to PD1 is only observed or a 2-3 minutes and then can't be detected, the situation for SHP2 becoming the same as it is for SHP1. If the kinetics are different in the cleaner systems that have now developed they should show this in a primary figure as this would be then different when what is reported previously.
We agree with the reviewer that pull down is evidence for binding. Indeed, in most, if not all of our assays, our results with pull down were consistent with those in the microcluster imaging. As suggested by the reviewer, we will check through the manuscript and ensure the language is accurate and consistent. In our recent study (Xu et al., JCB, 2020, PMID: 32437509), we conducted a side-by-side comparison of SHP2 and SHP1 recruitment kinetics to PD-1 in a similar system as the current study. Both microcluster imaging and co-IP assays showed that PD-1:SHP2 association lasted at least 10 minutes, whereas PD-1:SHP1 recruitment was nearly undetectable. The duration of PD- 1:SHP2 association was in good agreement with Takashi Saito’s finding in CD4+ mouse T cells (Yokosuka et al., JEM, 2012, PMID: 22641383). Regardless the somewhat different kinetics in different studies, SHP2 recruitment was transient, as pointed out by the reviewer. We believe that some other effectors contribute to PD-1 inhibitory signaling. In supportive of this notion, we recently found that PD-1 remains partially inhibitory in CD8+ T cells deficient in both SHP1 and SHP2 (Xu et al., JCB, 2020).
The gap in this study is lack of any functional analysis. The Jurkat model could be quite useful as they have a relatively clean system for asking if the transient binding of SHP1 to PD1 has any functional impact, which they have not yet followed through on. Does PD-1 recruited SHP2 have any impact on function after the 5 minutes? Furthermore, the authors need to keep in mind that mice deficient in SHP2 respond to anti-PD1 checkpoint therapies (Rota, G., Niogret, C., Dang, A. T., Barros, C. R., Fonta, N. P., Alfei, F., Morgado, L., Zehn, D., Birchmeier, W., Vivier, E., & Guarda, G. (2018). Shp-2 Is Dispensable for Establishing T Cell Exhaustion and for PD-1 Signaling In Vivo. Cell Rep, 23(1), 39-49. https://doi.org/10.1016/j.celrep.2018.03.026). This is an important issue to discuss in light the the very interesting binding analysis the authors have performed. But I think the functional analysis can be part of a future paper.
In our recent publication (Xu et al. JCB, 2020, PMID: 32437509), we found that deletion of SHP1 from Jurkat cells had little, if any effect on PD-1 mediated suppression of IL-2 production. As the reviewer alluded to, we did observe SHP2 dissociation from PD-1 after 10 minutes, so the question of whether and how PD-1:SHP2 complex influence T cell function in a longer term is a great one. We currently are pursuing a hypothesis that there is a SHP2-independent mechanism of PD-1 inhibitory function, and indeed, in our recent study (Xu et al. JCB, 2020, PMID: 32437509), we found that PD-1 retains its partial inhibitory function in SHP1/SHP2 double knockout murine primary T cells. These results are consistent with the in vivo data by Rota et al. cited by the reviewer. We will also briefly discuss this point in a revised manuscript.
I would suggest that the title be modified slightly from "SHP1/SHP2 discrimination" to "differential SHP1/SHP2 interaction" and leave discussion of discrimination until they have the functional data integrated over times that are relevant to T cell transcriptional regulation (1-2 hrs). The functional analysis can be in another paper, but it would be interesting to have a paragraph in the discussion raising the outstanding issues beyond stable binding detected by the pull-down and microcluster recruitment experiments- what are the implications for function. Could the transient interactions in the noise of the steady state and equilibrium measurements be functional?
We thank the reviewer for the suggestion, even though reviewer #3 felt that our current title is appropriate. We will be happy to change the title at the editors’ discretion.
I would summarise that the work is outstanding as biochemistry and biophysics and it should be published nearly as is. I'm suggesting minor revisions in that the changes are just to text, but I think this is important and somewhat nuanced aspect of the paper that will make it even more helpful to readers.
We appreciate the positive and insightful comments!
Reviewer #1 (Significance):
The authors generate a detailed descriptive data set about the component interaction of SHP1 and SHP2 SH2 domains with PD1 and BTLA intracellular domains. They then test hypotheses generated from the descriptive data set to better define the nature of the interactions and why PD1 recruits primarily SHP2, while BTLA mainly recruits SHP1. PD1 is a major driver or the cancer immunotherapy revolution and SHP2 is the major candidate for a signalling effector of PD1. This paper can become the reference paper for the specificity and engineering of this interaction, which will make it highly significant in a very active and still expanding field.
Referee Cross-commenting
I still feel that "discrimination" has a functional/activity connotation that is not addressed at all in this paper, but can be addressed. I'm happy to have the suggestion stand and let the authors decide. They need to live with it once its published. Another suggestion- the citations on regulation are mostly old. A good recent paper is Pádua, R. A. P., Sun, Y., Marko, I., Pitsawong, W., Stiller, J. B., Otten, R., & Kern, D. (2018). Mechanism of activating mutations and allosteric drug inhibition of the phosphatase SHP2. Nature Communications, 9(1),
We believe that some of the functional questions raised by this reviewer, including the SHP1 and SHP2 contribution in PD-1 signaling, was addressed in our recent publication (Xu et al., JCB, 2020). Using SHP1 KO and SHP2 KO T cells, we showed that PD-1 inhibitory function is contributed by SHP2, but very little if any by SHP1. Thus in the current study, we focus on the mechanism behind the striking SHP2 preference by PD-1. We thank this reviewer for suggesting this excellent reference. We will cite this reference in the revised manuscript.
Reviewer #2 (Evidence, reproducibility and clarity):
In this study, Xu and co-workers investigate the biophysical nature of the interaction between the structurally-related non-transmembrane PTPs Shp1 and Shp2 with the ITIM/ITSM-containing inhibitory receptors PD-1 and BTLA using cell-based, biochemical, biophysical and domain swapping assays. The primary aim being to better understand how these receptors discriminate between binding Shp1 and/or Shp2, and the orientation of Shp1 and Shp2 engagement. These are major unresolved questions in the field that the authors go some way to addressing in a methodical, rigorous, clear and concise manner. Findings are convincing, correlate well with previous findings and internally, and are complemented with excellent schematics, making it easy to comprehend.
Major comments
The authors focus primarily on binding affinities to explain differential binding of Shp1 and Shp2 by PD-1 and BTLA ITIMs and ITSMs, but this is only part of the story. Avidity, compartmentalization, stoichiometry of kinases, and relative abundance of Shp1 and Shp2 are also important aspects of the discriminatory mechanism that are not addressed. Competition assays would go some way to addressing the latter point and should be at least be considered and discussed.
We agree that various parameters mentioned by this reviewers, such as compartmentalization and relative expression levels would be a concern for purely cell-free assays such as SPR, however, we feel that our cell-based assays already integrate these parameters. This is also precisely the reason why we chose to examine the recruitments of Shp1/2 in a cellular context instead of a purely cell-free system.
Regarding the competition, we have confirmed our key results in both WT and SHP2 KO background, with or without the potential competition from endogenous SHP2, suggesting that competition might not be a dominant mechanism for the recruitment specificity we observed.
Similarly, authors do not address how distortion of the pY binding pocket of Shp1 and Shp2 nSH2 domains in the auto-inhibited conformation is released, allowing the domain to engage with phopho-ITIM/ITSM. Again, this should be at least discussed. Current binding studies do not address this issue.
We feel that the overall recruitment to the PD-1 microclusters as we observed in cells already integrate this auto-inhibition mechanism of Shp1 and Shp2, because we used full length proteins. We do agree with the reviewer that future studies are warranted to address the contributions of each mechanism, including auto-inhibition, concentration, competition, etc., to the overall recruitment. This might require careful and extensive biophysical analyses coupled with mathematical modeling.
Minor comments:
Phosphorylation should be indicated in schematic representations in Figures 3, 6 b, c.
We thank the reviewer for this advice, we will indicate phosphorylation in the revised figure 3.
Cellular and physiological significance should be further discussed, as well as broader implications of findings to other ITIM/ITSM-containing receptors in other lineages.
We will further discuss this as suggested.
Reviewer #2 (Significance)
Findings from this study advance our knowledge of how inhibitory checkpoint regulatory receptors discriminate between Shp1 and Shp2, which has important implications for understanding how the unique biochemical, cellular and physiological functions of these receptors and phosphatases are dictated. Indeed, findings lay the foundation for a universal mechanism, that may apply to all ITIM/ITSM receptors in other cell lineages, and perhaps novel ways of targeting these interactions therapeutically.
Compare to existing published knowledge
Although largely correlative with previous studies, findings from this study start to fill major gaps in our knowledge of these biochemical processes, in a highly rigorous, concise and clear manner. Findings from previous studies were more 'piecemeal', whereas this study consolidates and advances important nuances of these interactions. Moreover, it lays the foundation for further structural, physiological and therapeutic studies.
Audience
The immune receptor signaling community and beyond, including any lineage in which ITIM/ITSM-containing receptors play a major role in regulating cellular responses.
Your expertise
ITIM/ITSM-containing receptors, kinase-phosphatase molecular switches, cellular reactivity to extracellular matrix proteins
Referee Cross-commenting
Generally agree with reviewer's comments. Constructive overall and fair. Although I was thinking additional competition experiments, I do not think necessary. Over the top for this study. Hence, 1 month should suffice to revise accordingly.
We thank this reviewer for the excellent comments and understanding!
Reviewer #3 (Evidence, reproducibility and clarity):
Summary:
Inhibitory immune receptors containing ITIMs function through recruiting the phosphatases SHP-1 and SHP-2. SHP-1 and SHP-2 are remarkably similar yet have different roles in vivo. How can ITIM-containing immune receptors specifically recruit SHP-1 or SHP-2? In this paper, Xu et al ask how SHP-1 vs SHP-2 specificity is achieved. They use very thorough biochemical assays to measure the affinity of SHP-1 and SHP-2 for various ITIM/ITSMs and finally pin point some key amino acids that switch an ITIM/ITSM from SHP-2 to SHP-1 specificity. The in vitro biochemical assays are augmented by in cell assays that support their conclusions. Overall, this paper is an incredibly elegant and straight forward paper addressing how SHP-1/SHP-2 specificity is achieved.
Major Comments: none
Minor Comments:
- Could the western blots in Figure 1 be quantified as the western blots in other figures?
We will quantify the western blots in Figure 1 as suggested in the revised manuscript.
- The data that the y+1 reside is essential for SHP-1/2 specificity is very convincing. We are curious if the other residues of the ITIM/ITSM also contribute to this specificity, albeit less potently. The PD-1 G224A mutant is still less potent than the PD-1 BTLA ITIM swap, suggesting that while the y+1 position is most important, the other residues contribute some specificity. The authors also included data on a PD-1 variant with the BTLA ITIM A224G mutation (8f), which is slightly better at recruiting SHP-1 than the PD-1 ITIM. It may be worth mentioning this data in the text of the paper as well as displaying it in the figure.
The reviewer raised an excellent point, yes, our data does suggest that other pY-flanking residues within the ITIM also contribute to SHP1 binding. However, the pY+1 residue replacement produced the strongest effect as the reviewer noted. In the revised manuscript, we will acknowledge the potential contributions of other residues.
- A brief introduction to ITIM vs ITSM in the introduction of the paper may be helpful background for readers. For example, ITIM receptors are reasonably well known but how ITSM functionally differs is probably less well known.
We will rewrite the introduction about ITIM and ITSM for better clarity.
- Although not the major focus of the paper, broadening out this SHP-1/2 specificity to other immune receptors in the discussion is fascinating. (a) The authors find that a Valine, Leucine, or Isoleucine in place of the Alanine in y+1 is very close to equivalent, yet the A is highly conserved. The authors speculate that there may be an advantage to sub-maximal SHP-1 affinity because it is more easy to regulate. I think this is reasonable speculation but a little unsatisfying given the very small observed difference in SHP-1 binding. If the authors have additional thoughts, I would be interested to hear them. (b) The authors note that PD-1 is the only ITIM with a glycine in the Y+1 position. Are there other receptors that function primarily through SHP-2, and how might they achieve this specificity?
Response to a: Even though valine, leucine or isoleucine did not produce a striking enhancement in Shp1 recruitment over alanine, the differences were statistically significant. In fact, when we performed these point mutations at a BTLA ITIM background, valine, leucine or isoleucine markedly enhanced the SHP1 recruitment (see unpublished data below). We speculate that other pY-flanking residues in BTLA, as this reviewer alluded to above, creates an environment that amplifies the differences. The strong sensitivity on pY+1 residue, as observed in BTLA, might be true for other SHP1-recruiting receptors too. If they were to have leucine or isoleucine at the pY+1 position of ITIM, they may recruit too much SHP1 that presumably decreases the fitness/growth of the cells. We propose to show this unpublished data as a supplemental figure in the revised manuscript. We will also discuss the potential contributions of other pY-flanking residues as this reviewer suggested.
{{images cannot be rendered at this time in reply letters}}
Response to b: Among the several receptors that we tested, PD-1 is the only receptor that exhibited no recruitment of SHP1. The lack of SHP1 recruitment is also true for murine PD-1, which has a glutamate residue (charged) at Y+1 position. In addition, earlier work reported that PECAM1 also selectively recruits SHP2, but not SHP1. We have noted that PECAM1 contain a threonine (polar) at the pY+1 position of their ITIMs. Thus, their inability to recruit SHP1 is consistent with our model that a nonpolar residue at Y+1 position is required for strong SHP1 recruitment. We will discuss these points in the revised manuscript.
- Figure 9 b Val not Vla, Figure 3a - a legend for the color code may be nice (ie, 20-1000 nM) Thanks for catching this, we will fix the error in Figure 9b and provide the color code in Figure 3a in the revised manuscript.
Reviewer #3 (Significance):
Significance:
SHP-1 and SHP-2 play a critical role in regulating immune system function. In addition, the receptors recruiting these phosphatases (like PD-1) are important immunotherapy targets. Previously, the question of SHP-1/SHP-2 specificity has been primarily described for ITIM bearing receptors individually. Other studies have predicted consensus sequences for the tSH2 domains of SHP-1 or SHP-2, but not addressed the defining molecular characteristics of these consensus sites or how these could be combined on ITIM receptors to generate selectivity between these related phosphatases. This paper represents a significant step forward because it provides a unifying mechanism explaining how ITIM-bearing immune receptors specifically recruit SHP-1 or SHP-2. I expect this paper will be broadly interesting to biochemists, immunologists and cancer biologists.
Referee Cross-commenting
I generally think the other reviewers comments are reasonable and insightful. Together, they suggest no new experiments are necessary. As for the proposed title change, I prefer the authors title and find it to be justified given their data.
Reviewer #4 (Evidence, reproducibility and clarity):
In this manuscript, Xu and college performed an elaborate study to investigate the molecular basis of Shp1 and Shp2 discrimination by immune checkpoints PD-1 and BTLA. The paper is original, clear, and well written. I only have a few minor comments:
- Please label the molecular weights to all the western blots/IPs results.
We will label the molecular weights to all the blots in the revised manuscript.
- Please add scale bars to all the microscopy pictures.
We will add scale bars to all the microcopy images in the revised manuscript.
- For the SPR data, please add the fitting curves.
We thank the reviewer for the suggestion. However, we did not use the fitting curve to calculate the Kd, we plotted the maximum response as a function of concentration to determine the Kd. This is another well accepted method for Kd calculation. In fact, some of the SPR curves fit poorly with the existing algorithm. Thus, showing the fitting curve might distract the readers.
Reviewer #4 (Significance):
The strength of this paper relies on the details they dissected by using a series of mutagenesis screening experiments, which should be interesting to cell biologists and cancer immunologists.
Referee Cross-commenting
I think the other reviewer's comments are insightful and constructive, the suggested experiments are necessary and will improve the paper.
We thank this reviewer for the positive comments!
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Referee #4
Evidence, reproducibility and clarity
In this manuscript, Xu and college performed an elaborate study to investigate the molecular basis of Shp1 and Shp2 discrimination by immune checkpoints PD-1 and BTLA. The paper is original, clear, and well written. I only have a few minor comments:
- Please label the molecular weights to all the western blots/IPs results.
- Please add scale bars to all the microscopy pictures.
- For the SPR data, please add the fitting curves.
Significance
The strength of this paper relies on the details they dissected by using a series of mutagenesis screening experiments, which should be interesting to cell biologists and cancer immunologists.
Referee Cross-commenting
I think the other reviewer's comments are insightful and constructive, the suggested experiments are necessary and will improve the paper.
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Referee #3
Evidence, reproducibility and clarity
Summary:
Inhibitory immune receptors containing ITIMs function through recruiting the phosphatases SHP-1 and SHP-2. SHP-1 and SHP-2 are remarkably similar yet have different roles in vivo. How can ITIM-containing immune receptors specifically recruit SHP-1 or SHP-2? In this paper, Xu et al ask how SHP-1 vs SHP-2 specificity is achieved. They use very thorough biochemical assays to measure the affinity of SHP-1 and SHP-2 for various ITIM/ITSMs and finally pin point some key amino acids that switch an ITIM/ITSM from SHP-2 to SHP-1 specificity. The in vitro biochemical assays are augmented by in cell assays that support their conclusions. Overall, this paper is an incredibly elegant and straight forward paper addressing how SHP-1/SHP-2 specificity is achieved.
Major Comments:
none
Minor Comments:
- Could the western blots in Figure 1 be quantified as the western blots in other figures?
- The data that the y+1 reside is essential for SHP-1/2 specificity is very convincing. We are curious if the other residues of the ITIM/ITSM also contribute to this specificity, albeit less potently. The PD-1 G224A mutant is still less potent than the PD-1 BTLA ITIM swap, suggesting that while the y+1 position is most important, the other residues contribute some specificity. The authors also included data on a PD-1 variant with the BTLA ITIM A224G mutation (8f), which is slightly better at recruiting SHP-1 than the PD-1 ITIM. It may be worth mentioning this data in the text of the paper as well as displaying it in the figure.
- A brief introduction to ITIM vs ITSM in the introduction of the paper may be helpful background for readers. For example, ITIM receptors are reasonably well known but how ITSM functionally differs is probably less well known.
- Although not the major focus of the paper, broadening out this SHP-1/2 specificity to other immune receptors in the discussion is fascinating. (a) The authors find that a Valine, Leucine, or Isoleucine in place of the Alanine in y+1 is very close to equivalent, yet the A is highly conserved. The authors speculate that there may be an advantage to sub-maximal SHP-1 affinity because it is more easy to regulate. I think this is reasonable speculation but a little unsatisfying given the very small observed difference in SHP-1 binding. If the authors have additional thoughts, I would be interested to hear them. (b) The authors note that PD-1 is the only ITIM with a glycine in the Y+1 position. Are there other receptors that function primarily through SHP-2, and how might they achieve this specificity?
- Figure 9 b Val not Vla, Figure 3a - a legend for the color code may be nice (ie, 20-1000 nM)
Significance
SHP-1 and SHP-2 play a critical role in regulating immune system function. In addition, the receptors recruiting these phosphatases (like PD-1) are important immunotherapy targets. Previously, the question of SHP-1/SHP-2 specificity has been primarily described for ITIM bearing receptors individually. Other studies have predicted consensus sequences for the tSH2 domains of SHP-1 or SHP-2, but not addressed the defining molecular characteristics of these consensus sites or how these could be combined on ITIM receptors to generate selectivity between these related phosphatases. This paper represents a significant step forward because it provides a unifying mechanism explaining how ITIM-bearing immune receptors specifically recruit SHP-1 or SHP-2. I expect this paper will be broadly interesting to biochemists, immunologists and cancer biologists.
Referee Cross-commenting
I generally think the other reviewers comments are reasonable and insightful. Together, they suggest no new experiments are necessary. As for the proposed title change, I prefer the authors title and find it to be justified given their data.
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Referee #2
Evidence, reproducibility and clarity
In this study, Xu and co-workers investigate the biophysical nature of the interaction between the structurally-related non-transmembrane PTPs Shp1 and Shp2 with the ITIM/ITSM-containing inhibitory receptors PD-1 and BTLA using cell-based, biochemical, biophysical and domain swapping assays. The primary aim being to better understand how these receptors discriminate between binding Shp1 and/or Shp2, and the orientation of Shp1 and Shp2 engagement. These are major unresolved questions in the field that the authors go some way to addressing in a methodical, rigorous, clear and concise manner. Findings are convincing, correlate well with previous findings and internally, and are complemented with excellent schematics, making it easy to comprehend.
Major comments
The authors focus primarily on binding affinities to explain differential binding of Shp1 and Shp2 by PD-1 and BTLA ITIMs and ITSMs, but this is only part of the story. Avidity, compartmentalization, stoichiometry of kinases, and relative abundance of Shp1 and Shp2 are also important aspects of the discriminatory mechanism that are not addressed. Competition assays would go some way to addressing the latter point and should be at least be considered and discussed.
Similarly, authors do not address how distortion of the pY binding pocket of Shp1 and Shp2 nSH2 domains in the auto-inhibited conformation is released, allowing the domain to engage with phopho-ITIM/ITSM. Again, this should be at least discussed. Current binding studies do not address this issue.
Minor comments:
Phosphorylation should be indicated in schematic representations in Figures 3, 6 b, c.
Cellular and physiological significance should be further discussed, as well as broader implications of findings to other ITIM/ITSM-containing receptors in other lineages.
Significance
Findings from this study advance our knowledge of how inhibitory checkpoint regulatory receptors discriminate between Shp1 and Shp2, which has important implications for understanding how the unique biochemical, cellular and physiological functions of these receptors and phosphatases are dictated. Indeed, findings lay the foundation for a universal mechanism, that may apply to all ITIM/ITSM receptors in other cell lineages, and perhaps novel ways of targeting these interactions therapeutically.
Compare to existing published knowledge
Although largely correlative with previous studies, findings from this study start to fill major gaps in our knowledge of these biochemical processes, in a highly rigorous, concise and clear manner. Findings from previous studies were more 'piecemeal', whereas this study consolidates and advances important nuances of these interactions. Moreover, it lays the foundation for further structural, physiological and therapeutic studies.
Audience
The immune receptor signaling community and beyond, including any lineage in which ITIM/ITSM-containing receptors play a major role in regulating cellular responses.
Your expertise
ITIM/ITSM-containing receptors, kinase-phosphatase molecular switches, cellular reactivity to extracellular matrix proteins
Referee Cross-commenting
Generally agree with reviewer's comments. Constructive overall and fair. Although I was thinking additional competition experiments, I do not think necessary. Over the top for this study. Hence, 1 month should suffice to revise accordingly.
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Referee #1
Evidence, reproducibility and clarity
This paper explores an interesting problem of SHP1/SHP2 preferences of inhibitory immunoreceptors. The author are quick to point out that many of their individual data points confirm published results at some level, but the power of the paper is in the parallel analysis of both PD1, which is strongly biased towards SHP2 and BTLA, which is biased towards SHP1. This gives them the opportunity to test the predictions of descriptive experiment by making simple mutated receptors with swapped ITIM or ITSM domains.
The work is very well done and generally the authors are quite careful and precise about the language used to describe results, in general.
The results are quite striking in that the find plenty of evidence for transient interaction of SHP1 with PD1 based on the biophysical measurements, but don't detect the interactions in pull down or in "in cell" microcluster recruitment experiments. In describing the pull-downs they discuss the issue of dissociation during washing potentially missing interactions that are taking place. I would prefer that the pull down is fine evidence for binding, but lack of pull down is not evidence for lack of binding. They should double check that this language is consistent. Also, unless something has changed in the microcluster binding experiments, this in situ recruitment of SHP2 to PD1 is only observed or a 2-3 minutes and then can't be detected, the situation for SHP2 becoming the same as it is for SHP1. If the kinetics are different in the cleaner systems that have now developed they should show this in a primary figure as this would be then different when what is reported previously.
The gap in this study is lack of any functional analysis. The Jurkat model could be quite useful as they have a relatively clean system for asking if the transient binding of SHP1 to PD1 has any functional impact, which they have not yet followed through on. Does PD-1 recruited SHP2 have any impact on function after the 5 minutes? Furthermore, the authors need to keep in mind that mice deficient in SHP2 respond to anti-PD1 checkpoint therapies (Rota, G., Niogret, C., Dang, A. T., Barros, C. R., Fonta, N. P., Alfei, F., Morgado, L., Zehn, D., Birchmeier, W., Vivier, E., & Guarda, G. (2018). Shp-2 Is Dispensable for Establishing T Cell Exhaustion and for PD-1 Signaling In Vivo. Cell Rep, 23(1), 39-49. https://doi.org/10.1016/j.celrep.2018.03.026). This is an important issue to discuss in light the the very interesting binding analysis the authors have performed. But I think the functional analysis can be part of a future paper.
I would suggest that the title be modified slightly from "SHP1/SHP2 discrimination" to "differential SHP1/SHP2 interaction" and leave discussion of discrimination until they have the functional data integrated over times that are relevant to T cell transcriptional regulation (1-2 hrs). The functional analysis can be in another paper, but it would be interesting to have a paragraph in the discussion raising the outstanding issues beyond stable binding detected by the pull-down and microcluster recruitment experiments- what are the implications for function. Could the transient interactions in the noise of the steady state and equilibrium measurements be functional?
I would summarise that the work is outstanding as biochemistry and biophysics and it should be published nearly as is. I'm suggesting minor revisions in that the changes are just to text, but I think this is important and somewhat nuanced aspect of the paper that will make it even more helpful to readers.
Significance
The authors generate a detailed descriptive data set about the component interaction of SHP1 and SHP2 SH2 domains with PD1 and BTLA intracellular domains. They then test hypotheses generated from the descriptive data set to better define the nature of the interactions and why PD1 recruits primarily SHP2, while BTLA mainly recruits SHP1. PD1 is a major driver or the cancer immunotherapy revolution and SHP2 is the major candidate for a signalling effector of PD1. This paper can become the reference paper for the specificity and engineering of this interaction, which will make it highly significant in a very active and still expanding field.
Referee Cross-commenting
I still feel that "discrimination" has a functional/activity connotation that is not addressed at all in this paper, but can be addressed. I'm happy to have the suggestion stand and let the authors decide. They need to live with it once its published. Another suggestion- the citations on regulation are mostly old. A good recent paper is Pádua, R. A. P., Sun, Y., Marko, I., Pitsawong, W., Stiller, J. B., Otten, R., & Kern, D. (2018). Mechanism of activating mutations and allosteric drug inhibition of the phosphatase SHP2. Nature Communications, 9(1), 4507. https://doi.org/10.1038/s41467-018-06814-w .
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity):
This study reveals the role of WW-PLEKHAs (PLEKHA5, 6 and 7) in the basolateral targeting of copper (Cu) transporter ATP7A. The Authors suggest that the WW-PLEKHAs/PDZD11/ATP7A interaction directs Cu-induced trafficking of ATP7A to the basolateral surface of epithelial cells. Suppression of WW-PLEKHAs impairs basolateral delivery of ATP7A and causes increased intracellular Cu levels. On the contrary, WW-PLEKHAs do not seem to participate in the retrieval of ATP7A back to the Golgi once the Cu levels return to basal values. To support these notions the manuscript provides a substantial set of the data, which were achieved with a wide repertoire of methods. In my view, this manuscript could be of interest to a broad readership, ranging from cells biologists to medical doctors. However, further revision should address the concerns outlined below.
Major points:
- The Authors claim that at basal Cu conditions ATP7A resides in the TGN regardless of PDZD11 or WW-PLEKHAs depletion (Figs. 3, 4 and Fig. S6, S7). However, colocalization with TGN marker and its quantification are not shown. Thus, the colocalization of ATP7A with TGN marker (Golgin 97 should work in all cell types) has to be shown and its quantification (Pearson coefficient) has to be provided for control and all KO cells.
Response: We thank the Reviewer for this comment. We plan to carry out the IF colocalization of ATP7A with Golgin97 and quantifications for WT and KO clonal lines at basal Cu conditions.
- Along the same line, ATP7A colocalization with TGN marker and its quantification also has to be conducted for the Cu washout experiments.
Response: We plan to carry out the IF colocalization of ATP7A with Golgin97 and quantifications for WT and KO clonal lines for the Cu washout conditions.
- The authors say that upon addition of Cu ATP7A labeling was detected along lateral contacts, and near the apical and basal plasma membranes (Fig. 3B, WT). Here again "near apical" localization of ATP7A has to be clarified. This could either represent the ATP7A pool that still remains in the Golgi (which is usually close to apical surface in polarized epithelial cells) or the ATP7A pool delivered to the apical membrane of the cells. However, apical targeting of ATP7A would be odd considering previously published data that shows basolateral localization in polarized epithelial cells. Thus, the authors have to show whether "apical" ATP7A overlaps with TGN marker or with an apical marker (Gp135).
Response. This Reviewer is correct. Effectively we believe that the localization of ATP7A that we observe in cysts is not apical, but sub-apical, as shown for the localization of PLEKHA5, where colocalization with the apical marker gp135 clearly shows a different localization (Fig. 2I).
Therefore, we will carry out co-localization of ATP7A with gp135 in MDCK cells (the monoclonal antibody does not work on mCCD cells) and the labeling of the micrographs in Fig. 3B and 4B will be revised (sub-apical instead of apical). The labeling of PLEKHA5 sub-apical pool will also be revised (sub-apical and not apical) in Fig. 2.
- PDZD11 or PLEKHA6/7 KOs lead to an ATP7A pattern, which looks like pretty large scattered vesicles that do not overlap with basolateral marker. What are these round ATP7A structures, endosomes? Colocalization assessments with EEA1 (early endosomes), VPS35 (sorting endosome) and LAMP1 (late endosomes) would be needed to clarify this. Alternatively, these vesicles could represent a fragmented Golgi with ATP7A inside. To establish this, labelling with TGN marker at these conditions is required.
Response: We thank the Reviewer for this comment. To clarify the nature (endosomes, Golgi, etc) of the membrane vesicles where ATP7A is localized in KO lines we will carry out double IF colocalization of ATP7A with either Golgin97 or early/sorting (which are mostly overlapped) endosome or the late endosome markers.
- Biotinylation experiments. The Authors say that KO of either PDZD11, or PLEKHA7, or both PLEKHA6 and PLEKHA7, but not PLEKHA6 alone, decreased ATP7A levels at the basolateral surface of mCCD cells (Fig. 3G), while a small decrease in the basolateral levels of ATP7A is observed in PLEKHA5-KO, but not PLEKHA6-KO MDCK cells (Fig. 4G). Honestly, it is tough to see this. In Fig. 4G all ATP7A bands in the biotinylated fraction look similar. In Fig. 3G, the P11 and P6/7 KO bands of biotinylated ATP7A might be a bit less intense than in WT, while the P6 KO signal looks even more intense that WT. More convincing blots with quantification have to be provided for both figures.
Response: We will carry out additional immunoblots and quantifications of the biotinylation experiments results.
- Along the same line. Why was apical biotinylation of ATP7A not included? It absolutely should be done to understand whether any KO induces apical mistargeting of ATP7A.
Response: The levels of ATP7A at the apical surface upon basal or elevated copper are negligible and not physiologically relevant, as established by previous biotinylation studies (for example Greenough et al AJP 2004, and Nyasae et al AJP-Gastrointest Liver Physiol 2007). We will carry out IF analysis of WT and KO cells with ATP7A and apical markers (ex. gp135) to clarify if the subapical labeling for ATP7A is or not on the apical membrane. Importantly, LESS, and not more subapical labeling is detected in KO lines (Fig. 3B, Fig. 4B), as we pointed out in the results section. Therefore, the KO lines do not show increased apical (mistargeting of) ATP7A.
- Copper metabolism. The authors say that KO of either PDZD11 or PLEKHA6/7 results in higher Cu levels. What does this mean in terms of physiology and pathology? In the context of Menkes disease one has to show that this intracellular Cu increase is due to a reduction in Cu release from the cells. So, Cu release from the cells into medium has to be measured by ICP-MS or Cu64. On the other hand, it would be important to understand whether Cu accumulation in KO cells is toxic. To this end viability of KO cells should be tested in Cu dose-response experiments.
Response: The focus of this paper is the molecular mechanisms of ATP7A targeting to the BL plasma membrane, rather than a quantitative analysis of copper transport by and analysis of physiology/pathology of copper homeostasis ATP7A in our WT and KO cell lines. Our measurement of the intracellular copper using the CF4 probe was designed as a physiological readout to confirm that altered localization at the BL plasma membrane correlates with reduced copper extrusion, as it can be hypothesized. This said, to address this point, we plan to carry out an ICP-MS analysis of intracellular copper in selected WT and KO lines, after loading cells with different amounts of copper, and at different times after return to basal copper levels. CF4 and ICP-MS generally track, but they do measure distinct copper pools: CF4 measures exchangeable Cu pools while ICP-MS measures total Cu pools. We will also carry out a crystal violet analysis (see Gudekar et al, Scient. Reports, 2020) of the viability of WT and KO cells in the absence and presence of low or elevated copper levels, as suggested by the Reviewer.
- How critical is WW-PLEKHAs or PDZD11 deficiency in terms of Cu metabolism? Are there genetic disorders or mouse phenotypes associated with their loss of function? If yes, do these phenotypes include any impairment of Cu metabolism?
Response: To our knowledge, no genetic study has addressed the role of WW-PLEKHAs and PDZD11 in Cu metabolism in vivo. PLEKHA7-KO mice are viable and were not reported to display any phenotype consistent with grossly altered Cu metabolism (Popov et al 2015). Mice KO for either PLEKHA5 or PLEKHA6 or PDZD11 have not been described. However, if WW- PLEKHAs have redundant functions in the trafficking of ATP7A, one would expect that mutation/KO of only one of them may not yield a significant phenotype. Furthermore, we cannot exclude that additional PDZ-containing proteins may participate in the trafficking of ATP7A, compensating a pathological or experimental loss of PDZD11. So, answering this question will require to generate single, double and triple KO mice for WW-PLEKHAs, and carry out a detailed analysis of in vivo Cu metabolism. This is beyond the scope of this paper. The text of the Discussion will be revised to address this comment.
- Discussion. Could PH domains of WW-PLEKHAS be involved in their basolateral localization, thereby generating a targeting patch for ATP7A? Some publications suggest that the basolateral membrane might be enriched in specific PIPs, which in turn generates a favorable environment for some PH domains. Is this the case for PH domains of WW-PLEKHAS?
Response: This is an interesting hypothesis that should be investigated in future studies (lipidomic analysis of KO lines, overexpression studies, etc), but is outside of the scope of the present manuscript.
Minor points:
- Fig. 6C. CFP-HA is a negative control but still gives a band (although of lower intensity). So how can one be sure that other interactions are specific? This is particularly worrying because the quantification shows a very minor (less than 1.5) increase in the intensity of bands corresponding to specific interactors.
Response: CFP-HA is used as a “negative control” 3_rd _protein, added to bait (GST-PDZD11) and prey (GFP-ATP7A-Cter) (Fig. 6C). The IB shows that in the presence of CFP-HA the bait binds the prey, which is in agreement with the previously reported interaction between PDZD11 and the C-terminal region of ATP7A (Stephenson et al JBC, 2005). The point of the Figure is to show that the interaction between bait and prey is enhanced in the presence of HA-tagged WW- PLEKHAs (again, CFP-HA is the negative control). We agree that the increase is not huge, but it is nevertheless statistically significant, based on several experiments (Fig. 6E).
- Page 11. The result section title "WW-PLEKHAs promote PDZD11 binding to ATP7A through PDZD11 (Figure 6)" does not sound right and has to be corrected.
Response: The text was revised ("WW-PLEKHAs promote PDZD11 binding to ATP7A”).
Reviewer #1 (Significance):
Delivery of copper transporter ATP7A to the basolateral surface of epithelial cells is of great importance for maintenance of copper metabolism and, hence for human health in general. Impairment of this process in enterocytes causes fatal Menkes disease. However, the mechanisms driving basolateral targeting of ATP7A remained poorly characterized. This study provides a significant advance in our understanding of these mechanisms and opens new avenues for investigation of how WW-PLEKHAs/PDZD11-mediated targeting of ATP7A might be affected in the context of inherited disorders of copper metabolism.
Reviewer #2 (Evidence, reproducibility and clarity):
This manuscript uncovers new PDZD11 interactors that participate in trafficking of the copper transporter ATP7A from the Golgi/TGN to the cell periphery in response to high copper concentrations. These interactors named PLEKHA5, PLEKHA6, and PLEKHA7 interact with the N-terminal Pro-rich domain of PDZD11 through their WW domains. As PDZD11 interacts with the C-terminal region of ATP7A, the authors investigated the hypothesis that WW-PLEKHAs are required for copper-induced relocalization of ATP7A from the TGN to the plasma membrane where it functions in copper efflux. In vitro pull down experiments verified the formation of ATP7A-, PLEKHAs-, and PDZD11-containing complexes. Using using CRISPR/Cas9 technology, the authors have generated PDZD11-, PLEKHA5-, PLEKHA6-, and PLEKHA6/7-KOs cell lines.
Cells lacking one (or more) of these proteins were examined by microscopy with respect to their ability of targeting ATP7A to the cell periphery in response to copper. Abnormal trafficking of ATP7A in these mutant cell lines (PDZD11-, PLEKHA5-, PLEKHA6-, PLEKHA7-, and PLEKHA6/7-KOs) presumably prevented copper efflux since elevated intracellular copper was detected using the fluorescent copper probe CF4.
Although it is difficult to read across the article's figures and supporting figure files (going back- and-forth repeatedly), the manuscript is generally clear and well written, and the results seem well documented accompanied by a tremendous amount of work.
Comments.
- Two-hybrid screen occurs in the nucleus. How the authors could explain the fact that the use of PDZD11 as a bait exhibited an interaction with PLEKHA5 and PLEKHA6 (as well as PLEKHA7) in this system? Microscopic analysis of PLEKHA5 showed a cytoplasmic submembrane localization with E-cadherin, whereas PLEKHA6 exhibited a localization along the plasma membrane at apical junctions. In the case of PLEKHA7, it is an adherens junction protein. Furthermore, these three proteins are quite big (1116, 1297, and 1121 AAs, respectively) with their WW regions at their N termini, which involved the expression of very long cDNAs fused to the TA domain. As truly membrane-associated proteins, isn't surprising that a two hybrid approach worked?
Response: We carried out several Y2H screens with a number of different baits, and we have always validated the physiological significance of the high score interactions (Pulimeno et al JBC 2011, Guerrera et al, 2016 JBC, and other unpublished data). So, it is an approach that reliably works very well. The Hybrigenics human placenta library that we used contains fragments of proteins, not the full-length proteins. Fig. 1A shows the preys identified with the Y2H using PDZD11 as a bait. The preys that were found comprise only the N-terminal regions of WW- PLEKHAs, not the FL proteins.
- Fig. 1C, what are the 4 bands seen for the second blot (anti-HA) in lines 1, 2, 9 and 10? The blot was cut in a way that not enough of the membrane can be evaluated. Why using Ponceau for GST-baits and not using anti-GST antibodies? It would be much better having an uniform method (Western blot assays) to show the data.
This latter comment is true for Fig 1D, E, and Fig 6.
Response: The 4 bands seen for the second blot (anti-HA) in lanes 1, 2, 9 and 10 are non- specific cross-reaction of the antibodies with the baits, that are present in high concentration (and present also where there is no CFP-HA, in lanes 1 and 9). The preys can be identified on the basis of their molecular size. For example, no CFP-HA prey is detected, since its size is intermediate between the baits, thus the negative control is validated. We use Ponceau for 2 reasons: 1) Ponceau can detect very well baits on nitrocellulose membranes; 2) to use GST antibodies we would need to cut the membranes. But cutting membranes is not possible when the size of some preys (in this case, the negative control) is in the same range of sizes as the baits. Thus, if we used anti-GST antibodies we would have to strip and re-probe the membranes, which is not optimal in our experience to elicit good signals.
- Fig 1B, why Caco-2 cells? All the other experiments were conducted with other cell lines such as mCCD and MDCK. Using different cell lines could give different results.
Response: We used Caco2 cells because the Y2H was carried out with a human bait on a human placental library, and Caco2 are human cells. We also tried to use MDCK cells, but the efficiency of the IP was lower.
- Fig 1D, it is unclear whether the GST-PDZD11 fusion protein (bait) was present or not when used in pull down assays with GFP alone. This is a clear disadvantage of Ponceau, immunoblot would be much better to use.
Response: The labeling by Ponceau is not optimal in one image (Fig. 1D), probably due to a problem of transfer. But a clearer image for the same pulldown with the same bait is shown in the bottom panel of Fig. 1E (where we show 3 PDZD11 baits, FL, N-term and delta-24), and it clearly shows good normalization of baits. We stain baits with Ponceau for normalization.
- In Fig 3A, under basal copper conditions, microscopic image of the PLEKHA6/7-KO seems indicate a distinct pattern of localization for ATP7A in comparison to that of WT. However, this difference does not seem to be highlighted in Fig 3E.
Response: We will re-examine all the micrographs used for the quantification and integrate the data with the results of the colocalization between ATP7A and TGN marker. This should allow us to establish whether there is a dissociation of ATP7A labeling from TGN marker labeling in KO cells, or else a fragmentation of the TGN in the double-KO mCCD cells.
In Figs 3F and 4F, what was the method for quantification?
Response: The methods for quantifications are described in the “Image quantification” section of the Methods. We will add new data about the quantification of co-localization of ATP7A with TGN and endosomal markers.
Along these lines, what is the copper concentration under basal conditions? How much copper was used for elevated copper conditions and what was the time of treatment?
Response: Basal conditions refers to normal cell culture medium (“Cell culture” section of the Methods), and elevated copper is 315 µM of CuCl2 dissolved in culture medium. Cells were treated for 4hr (MDCK) or 5hr (mCCD) when cells were cultured on Transwells, overnight in the case of cysts.
- Is there any evidence for Atp7A-PDZD11-PLEKHAs association in vivo? Do the authors have assessed these protein-protein interactions using methods such as bimolecular fluorescence in cells?
Response: We have attempted co-IP experiments with endogenous proteins, but they were inconclusive, probably due to the different extraction conditions required to solubilize membrane (ATP7A) and cytoplasmic (WW-PLEKHAs, PDZD11) proteins, and a disassembly of the complex under the conditions required to solubilize ATP7A. We have not tried bimolecular fluorescence, but for the revision we plan to carry out Proximity Ligation Assay (PLA) experiments, which in our hands are very effective in assessing physiological proximity of proteins in cells. Our pulldown experiments however provide evidence that the three proteins form a complex, and that WW- PLEKHAs enhance the interaction between PDZD11 and ATP7A (Fig. 6C-E). This is a mechanism that we have shown occurs also for the complex between PLEKHA7, PDZD11 and Tspan33 (Shah et al, 2018 Cell Rep, Rouaud et al, 2020 JBC).
- In Fig 5, do the authors have verified the mRNA (or/and protein) steady-state levels of metallothioneins? Probing whether metallothioneins are induced would strongly reinforced their conclusion as to whether an increase intracellular copper levels occurred in PDZD11-, PLEKHA5-, PLEKHA6-, PLEKHA7-, and PLEKHA6/7-Kos cell lines.
Response: We thank the Reviewer for this comment. In the revision we will carry out RT-PCR analysis of the levels of expression of mRNAs for Metallothioneins I and II.
- In Fig 6E, what was the method for quantitative immunoblot assays? Have you used an Odyssey infrared imaging system (Li-Cor). What was the loading (internal) control under the same analytical method?
Response: The Li-Cor imaging system was used to capture the signals, and intensities were measured in Image Studio Lite program (Li-cor). Signals from the prey (C-terminus of ATP7A) were normalized to signals from the bait (GST-PDZD11) which were used as loading control.
- In the case of the manuscript section entitled " PLEKHA5, PLEKHA6 and PLEKHA7 show distinct localizations in cells and tissues and define cytoplasmic...", (pages 5 to 7) the reader would benefit having a Table that would summarize all the data. It would be more understandable.
Response: We thank the Reviewer for this suggestion. We will include a Table in the revision.
- Do PDZD11, PLEKHA5, PLEKHA6, and PLEKHA7 proteins exist as multiple isoforms? If that is the case, for each of them, are they exhibiting the same tissue-specific expression profiles as shown in Fig S3? For each protein, if different isoforms exist, perhaps some of them participate in a different way for the targeting of ATP7A?
Response: No PDZD11 isoforms are known, but 15, 5, and 9 different protein-coding transcripts are reported (ensemble.org) for PLEKHA5, PLEKHA6 and PLEKHA7, respectively, the largest ones being the WW-containing transcripts. We focused exclusively on the WW-containing isoforms of PLEKHAs because PDZD11 binds to the WW domains, and the Y2H identified only the WW-containing isoforms of PLEKHA5, PLEKHA6 and PLEKHA7. The observation that the phenotype of PDZD11-KO cells is similar to that of either PLEKHA6-KO, PLEKHA7-KO or double-KO mCCD cells suggests that PLEKHA5, PLEKHA6 and PLEKHA7 WW-containing isoforms act in a complex with PDZD11. This is consistent with the previous observations that highlight a role of the C-terminal region of ATP7A in regulating its traffic, and the binding of the same region to PDZD11. However, we cannot exclude that PLEKHA5/6/7 isoforms that lack the WW domains could participate in the regulation of the targeting of ATP7A, through other, PDZD11-independent mechanisms. The text of the Discussion will be revised to clarify this point.
- Is it known whether PDZD11, PLEKHA5, PLEKHA6, and PLEKHA7 proteins participate in the copper-regulated trafficking of the ATP7B (Wilson) protein? In Fig S3, it is shown that they are expressed in liver, with PLEKHA7 exhibiting a slower migration (protein modification?). Alternatively, are they strictly involved in the regulation of ATP7A (Menkes)? Could the authors discuss about it?
Response: ATP7B lacks the PDZ-binding motif that is responsible for PDZD11 binding, and the C-terminus of ATP7B does not interact with PDZD11 (AIPP1) by beta-galactosidase assays in yeast, unlike ATP7A (Stephenson et al, JBC 2005). For this reason, ATP7B is not expected to be regulated by PDZD11 and WW-PLEKHAs. However, analysis of the localization of ATP7B in our cell lines could be done in future studies. The text of the Discussion will be revised to make this point.
- The proposed model in Fig 7 is unclear illustrating a nucleus that consumes a lot of space while it is not involved in the proposed mechanism. Cellular proteins that are involved in the proposed mechanism should be bigger and their interactions that lead to formation of protein complexes must be better illustrated as a function of copper availability.
Response: The model of Fig. 7 will be re-drawn to take into account these suggestions.
Typo. Line 320: remove "or" and replace it by "and" : ...both PLEKHA6 and PLEKHA7 (Fig. 5A-D).
Typo. Line 329: remove (Figure 6) in the title.
Response: The typos were corrected.
Reviewer #2 (Significance ):
This study represents a significant advanced in the copper field.
Reviewer #3 (Evidence, reproducibility and clarity):
Summary
The authors identified some major interesting findings including the key role of WW-PLEKHAs (PLEKHA5, PLEKHA6, PLEKHA7) in the recruitment of PDZD11 targeting ATP7A to the cell periphery in response to elevated copper. Generating the antibodies against PLEKHAs and PDZD11 and various knock out cell lines and validating their expression in these cell lines and tissues is innovative. Further, the authors showed that copper dependent WW-PLEKHAs and PDZD11 regulate the localization and function of ATP7A to modulate cellular copper homeostasis.
Major comments:
We are in agreement with the manuscript conclusions. Based on the presented studies, the authors propose the in-vivo role of WW-PLEKHAs and PDZD11 in ATP7A trafficking, and how microtubule dynamics and trafficking machinery regulate ATP7A localization. Additionally, investigating the effects of the cell membrane trimolecular complexes ATP7A-PDZD11-WW- PLEKHA on elevated copper would be impactful.
Additional notes:
- Figure 4, the authors provide excellent data and images showing localization of PLEKHA, PDZD11 and ATP7A within different cell lines. Nevertheless, showing PLEKHA, PDZD11 and ATP7A localization on membrane of the cell surfaces at elevated copper condition with cell fractionation technique and their interaction through co-immunoprecipitation (co-IP) could validate author's hypothesis. At least the authors should comment on this.
Response: As stated in the response to comment n.6 from Reviewer #2, we attempted co-IP experiments with endogenous proteins, which were inconclusive. Our pulldown experiments provide evidence that the three proteins form a complex, and that WW-PLEKHAs enhance the interaction between PDZD11 and ATP7A (Fig. 6C-E). This is a mechanism that we have shown occurs also for the complex between PLEKHA7, PDZD11 and Tspan33 (Shah et al, 2018 Cell Rep, Rouaud et al, 2020 JBC). We plan for the revision to carry out Proximity Ligation Assay (PLA) experiments, which in our hands are very effective in assessing proximity of proteins in cells, when co-IPs are technically difficult or impossible.
- Figure 5, Alternatively, intracellular copper levels by ICPMS in the cell lines would strengthen the results. As author's treated the cell lines with very high copper concentration, copper concentration dependent studies would be appreciated to verify how PLEKHA's and PDZD11 response depends on copper concentration
Also, the authors should clearly mention the number of replicates for each experiment and indicate in the figure legends.
Response. We will carry out ICP-MS to evaluate intracellular copper levels as a function of genotype. Depending on the results, we will carry out studies about the dose-dependence of the effects of copper. The number of replicates of the experiment will be mentioned in the Figure legend in the revised text.
Minor comments:
- Figure1B, co-IP efficiency is lower in Caco-2 cells, therefore endogenous levels of PLEKHA5, PLEKHA6 and PDZD11 in Caco-2 should be checked and shown. Mention the number of replicates for the experiments.
Response. Endogenous levels of proteins are shown in the Input lanes. The low levels of PLEKHA5 in Caco2 cells are consistent with the IB analysis of tissue lysates, showing relatively low levels in intestine (Fig. S3D). The number of replicates of the experiment will be mentioned in the Figure legend in the revised text.
- Figure 2A, as per result of 2A, E-cadherin labeling is missing. Figure 2M and 2N, author analyzed the co-localization of PLEKHA-5 in presence of nocodazole but not PDZD11. It would be interesting to see the PDZD11 as well after nocodazole treatment.
Response. E-cadherin-labelled panel will be added to Fig. 2A in the revision. We will also show the effect of nocodazole on the localization of PDZD11.
- The result section title for figure 6 (line 329) is misleading. Also, trimolecular complex PLEKHA's, PDZD11 and ATP7A membrane localization at elevated copper concentration could be shown by immunofluorescence, if possible.
Response. The title of the section was revised, to reflect more accurately the results of Figure 6. It is now “WW-PLEKHAs promote the binding of the C-terminal region of ATP7A to PDZD11”.
Triple IF colocalization of endogenous PLEKHAs, PDZD11 and ATP7A is not possible for 2 reasons: 1) PDZD11 antibodies can only reveal endogenous junctional (clustered) labeling (Guerrera et al JBC2016); the lateral and cytoplasmic labeling is too weak, and can only be appreciated upon overexpression of PDZD11, as shown in Fig. 2B-E (co-expression with selected WW-PLEKHAs highlights how each PLEKHA directs PDZD11 to a different pool). 2) Both antibodies against PDZD11 and ATP7A were raised in rabbits, which makes it technically impossible to do triple labeling. We will address the question of the existence of the ATP7A- containing trimolecular complex by PLA analysis (ATP7A+PDZD11 and ATP7A+WW-PLEKHAs)._
- General comment: it would be interesting to see the hypothesis and finding in mice model with copper accumulation (for example Atp7b KO mice) as PLEKHA's and PDZD11 are sensitive to copper concentration. Or at least the authors can comment on this future possibility.
Response. We agree with the Reviewer that mouse models could be useful to test the relevance of WW-PLEKHAs and PDZD11 as targets or effectors of copper-sensing mechanisms in vivo.
The text of the Discussion will be modified to envisage these possible future studies
Reviewer #3 (Significance):
In conditions including Menkes disease, occipital horn syndrome (OHS), and ATP7A-related distal motor neuropathy (DMN), characterized by altered intestinal copper metabolism, the new knowledge ATP7A associates with WW-PLEKHAs (PLEKHA5, PLEKHA6, PLEKHA7) and PDZD11 is an important finding for the study of copper homeostasis.
As ATP7A is structurally similar to ATP7B (60% homology), the current study opens the area of the research where WW-PLEKHAs (PLEKHA5, PLEKHA6, PLEKHA7) and PDZD11 could also play role in ATP7B trafficking to address not only Menkes disease but also Wilson disease and other diseases related to altered copper levels.
This is a well written and presented manuscript with excellent mechanistic work utilizing molecular imaging techniques and several confirmatory experiments. I recommend the manuscript to be accepted for publication with minor modifications.
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Referee #3
Evidence, reproducibility and clarity
Summary
The authors identified some major interesting findings including the key role of WW-PLEKHAs (PLEKHA5, PLEKHA6, PLEKHA7) in the recruitment of PDZD11 targeting ATP7A to the cell periphery in response to elevated copper. Generating the antibodies against PLEKHAs and PDZD11 and various knock out cell lines and validating their expression in these cell lines and tissues is innovative. Further, the authors showed that copper dependent WW-PLEKHAs and PDZD11 regulate the localization and function of ATP7A to modulate cellular copper homeostasis.
Major comments:
We are in agreement with the manuscript conclusions. Based on the presented studies, the authors propose the in-vivo role of WW-PLEKHAs and PDZD11 in ATP7A trafficking, and how microtubule dynamics and trafficking machinery regulate ATP7A localization. Additionally, investigating the effects of the cell membrane trimolecular complexes ATP7A-PDZD11-WW-PLEKHA on elevated copper would be impactful.
Additional notes:
- Figure 4, the authors provide excellent data and images showing localization of PLEKHA, PDZD11 and ATP7A within different cell lines. Nevertheless, showing PLEKHA, PDZD11 and ATP7A localization on membrane of the cell surfaces at elevated copper condition with cell fractionation technique and their interaction through co-immunoprecipitation (co-IP) could validate author's hypothesis. At least the authors should comment on this.
- Figure 5, Alternatively, intracellular copper levels by ICPMS in the cell lines would strengthen the results. As author's treated the cell lines with very high copper concentration, copper concentration dependent studies would be appreciated to verify how PLEKHA's and PDZD11 response depends on copper concentration Also, the authors should clearly mention the number of replicates for each experiment and indicate in the figure legends.
Minor comments:
- Figure1B, co-IP efficiency is lower in Caco-2 cells, therefore endogenous levels of PLEKHA5, PLEKHA6 and PDZD11 in Caco-2 should be checked and shown. Mention the number of replicates for the experiments.
- Figure 2A, as per result of 2A, E-cadherin labeling is missing. Figure 2M and 2N, author analyzed the co-localization of PLEKHA-5 in presence of nocodazole but not PDZD11. It would be interesting to see the PDZD11 as well after nocodazole treatment.
- The result section title for figure 6 (line 329) is misleading. Also, trimolecular complex PLEKHA's, PDZD11 and ATP7A membrane localization at elevated copper concentration could be shown by immunofluorescence, if possible.
- General comment: it would be interesting to see the hypothesis and finding in mice model with copper accumulation (for example Atp7b KO mice) as PLEKHA's and PDZD11 are sensitive to copper concentration. Or at least the authors can comment on this future possibility.
Significance
In conditions including Menkes disease, occipital horn syndrome (OHS), and ATP7A-related distal motor neuropathy (DMN), characterized by altered intestinal copper metabolism, the new knowledge ATP7A associates with WW-PLEKHAs (PLEKHA5, PLEKHA6, PLEKHA7) and PDZD11 is an important finding for the study of copper homeostasis.
As ATP7A is structurally similar to ATP7B (60% homology), the current study opens the area of the research where WW-PLEKHAs (PLEKHA5, PLEKHA6, PLEKHA7) and PDZD11 could also play role in ATP7B trafficking to address not only Menkes disease but also Wilson disease and other diseases related to altered copper levels.
This is a well written and presented manuscript with excellent mechanistic work utilizing molecular imaging techniques and several confirmatory experiments. I recommend the manuscript to be accepted for publication with minor modifications.
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Referee #2
Evidence, reproducibility and clarity
This manuscript uncovers new PDZD11 interactors that participate in trafficking of the copper transporter ATP7A from the Golgi/TGN to the cell periphery in response to high copper concentrations. These interactors named PLEKHA5, PLEKHA6, and PLEKHA7 interact with the N-terminal Pro-rich domain of PDZD11 through their WW domains. As PDZD11 interacts with the C-terminal region of ATP7A, the authors investigated the hypothesis that WW-PLEKHAs are required for copper-induced relocalization of ATP7A from the TGN to the plasma membrane where it functions in copper efflux. In vitro pull down experiments verified the formation of ATP7A-, PLEKHAs-, and PDZD11-containing complexes. Using using CRISPR/Cas9 technology, the authors have generated PDZD11-, PLEKHA5-, PLEKHA6-, and PLEKHA6/7-KOs cell lines. Cells lacking one (or more) of these proteins were examined by microscopy with respect to their ability of targeting ATP7A to the cell periphery in response to copper. Abnormal trafficking of ATP7A in these mutant cell lines (PDZD11-, PLEKHA5-, PLEKHA6-, PLEKHA7-, and PLEKHA6/7-KOs) presumably prevented copper efflux since elevated intracellular copper was detected using the fluorescent copper probe CF4.
Although it is difficult to read across the article's figures and supporting figure files (going back-and-forth repeatedly), the manuscript is generally clear and well written, and the results seem well documented accompanied by a tremendous amount of work.
Comments.
- Two-hybrid screen occurs in the nucleus. How the authors could explain the fact that the use of PDZD11 as a bait exhibited an interaction with PLEKHA5 and PLEKHA6 (as well as PLEKHA7) in this system? Microscopic analysis of PLEKHA5 showed a cytoplasmic submembrane localization with E-cadherin, whereas PLEKHA6 exhibited a localization along the plasma membrane at apical junctions. In the case of PLEKHA7, it is an adherens junction protein. Furthermore, these three proteins are quite big (1116, 1297, and 1121 AAs, respectively) with their WW regions at their N termini, which involved the expression of very long cDNAs fused to the TA domain. As truly membrane-associated proteins, isn't surprising that a two hybrid approach worked?
- Fig. 1C, what are the 4 bands seen for the second blot (anti-HA) in lines 1, 2, 9 and 10? The blot was cut in a way that not enough of the membrane can be evaluated. Why using Ponceau for GST-baits and not using anti-GST antibodies? It would be much better having an uniform method (Western blot assays) to show the data. This latter comment is true for Fig 1D, E, and Fig 6.
- Fig 1B, why Caco-2 cells? All the other experiments were conducted with other cell lines such as mCCD and MDCK. Using different cell lines could give different results.
- Fig 1D, it is unclear whether the GST-PDZD11 fusion protein (bait) was present or not when used in pull down assays with GFP alone. This is a clear disadvantage of Ponceau, immunoblot would be much better to use.
- In Fig 3A, under basal copper conditions, microscopic image of the PLEKHA6/7-KO seems indicate a distinct pattern of localization for ATP7A in comparison to that of WT. However, this difference does not seem to be highlighted in Fig 3E.
In Figs 3F and 4F, what was the method for quantification?
Along these lines, what is the copper concentration under basal conditions? How much copper was used for elevated copper conditions and what was the time of treatment?
- Is there any evidence for Atp7A-PDZD11-PLEKHAs association in vivo? Do the authors have assessed these protein-protein interactions using methods such as bimolecular fluorescence in cells?
- In Fig 5, do the authors have verified the mRNA (or/and protein) steady-state levels of metallothioneins? Probing whether metallothioneins are induced would strongly reinforced their conclusion as to whether an increase intracellular copper levels occurred in PDZD11-, PLEKHA5-, PLEKHA6-, PLEKHA7-, and PLEKHA6/7-KOs cell lines.
- In Fig 6E, what was the method for quantitative immunoblot assays? Have you used an Odyssey infrared imaging system (Li-Cor). What was the loading (internal) control under the same analytical method?
- In the case of the manuscript section entitled " PLEKHA5, PLEKHA6 and PLEKHA7 show distinct localizations in cells and tissues and define cytoplasmic...", (pages 5 to 7) the reader would benefit having a Table that would summarize all the data. It would be more understandable.
- Do PDZD11, PLEKHA5, PLEKHA6, and PLEKHA7 proteins exist as multiple isoforms? If that is the case, for each of them, are they exhibiting the same tissue-specific expression profiles as shown in Fig S3? For each protein, if different isoforms exist, perhaps some of them participate in a different way for the targeting of ATP7A?
- Is it known whether PDZD11, PLEKHA5, PLEKHA6, and PLEKHA7 proteins participate in the copper-regulated trafficking of the ATP7B (Wilson) protein? In Fig S3, it is shown that they are expressed in liver, with PLEKHA7 exhibiting a slower migration (protein modification?). Alternatively, are they strictly involved in the regulation of ATP7A (Menkes)? Could the authors discuss about it?
- The proposed model in Fig 7 is unclear illustrating a nucleus that consumes a lot of space while it is not involved in the proposed mechanism. Cellular proteins that are involved in the proposed mechanism should be bigger and their interactions that lead to formation of protein complexes must be better illustrated as a function of copper availability.
- Typo. Line 320: remove "or" and replace it by "and" : ...both PLEKHA6 and PLEKHA7 (Fig. 5A-D).
- Typo. Line 329: remove (Figure 6) in the title.
Significance
This study represents a significant advanced in the copper field.
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Referee #1
Evidence, reproducibility and clarity
This study reveals the role of WW-PLEKHAs (PLEKHA5, 6 and 7) in the basolateral targeting of copper (Cu) transporter ATP7A. The Authors suggest that the WW-PLEKHAs/PDZD11/ATP7A interaction directs Cu-induced trafficking of ATP7A to the basolateral surface of epithelial cells. Suppression of WW-PLEKHAs impairs basolateral delivery of ATP7A and causes increased intracellular Cu levels. On the contrary, WW-PLEKHAs do not seem to participate in the retrieval of ATP7A back to the Golgi once the Cu levels return to basal values. To support these notions the manuscript provides a substantial set of the data, which were achieved with a wide repertoire of methods. In my view, this manuscript could be of interest to a broad readership, ranging from cells biologists to medical doctors. However, further revision should address the concerns outlined below.
Major points:
- The Authors claim that at basal Cu conditions ATP7A resides in the TGN regardless of PDZD11 or WW-PLEKHAs depletion (Figs. 3, 4 and Fig. S6, S7). However, colocalization with TGN marker and its quantification are not shown. Thus, the colocalization of ATP7A with TGN marker (Golgin 97 should work in all cell types) has to be shown and its quantification (Pearson coefficient) has to be provided for control and all KO cells.
- Along the same line, ATP7A colocalization with TGN marker and its quantification also has to be conducted for the Cu washout experiments.
- The authors say that upon addition of Cu ATP7A labeling was detected along lateral contacts, and near the apical and basal plasma membranes (Fig. 3B, WT). Here again "near apical" localization of ATP7A has to be clarified. This could either represent the ATP7A pool that still remains in the Golgi (which is usually close to apical surface in polarized epithelial cells) or the ATP7A pool delivered to the apical membrane of the cells. However, apical targeting of ATP7A would be odd considering previously published data that shows basolateral localization in polarized epithelial cells. Thus, the authors have to show whether "apical" ATP7A overlaps with TGN marker or with an apical marker (Gp135).
- PDZD11 or PLEKHA6/7 KOs lead to an ATP7A pattern, which looks like pretty large scattered vesicles that do not overlap with basolateral marker. What are these round ATP7A structures, endosomes? Colocalization assessments with EEA1 (early endosomes), VPS35 (sorting endosome) and LAMP1 (late endosomes) would be needed to clarify this. Alternatively, these vesicles could represent a fragmented Golgi with ATP7A inside. To establish this, labelling with TGN marker at these conditions is required.
- Biotinylation experiments. The Authors say that KO of either PDZD11, or PLEKHA7, or both PLEKHA6 and PLEKHA7, but not PLEKHA6 alone, decreased ATP7A levels at the basolateral surface of mCCD cells (Fig. 3G), while a small decrease in the basolateral levels of ATP7A is observed in PLEKHA5-KO, but not PLEKHA6-KO MDCK cells (Fig. 4G). Honestly, it is tough to see this. In Fig. 4G all ATP7A bands in the biotinylated fraction look similar. In Fig. 3G, the P11 and P6/7 KO bands of biotinylated ATP7A might be a bit less intense than in WT, while the P6 KO signal looks even more intense that WT. More convincing blots with quantification have to be provided for both figures.
- Along the same line. Why was apical biotinylation of ATP7A not included? It absolutely should be done to understand whether any KO induces apical mistargeting of ATP7A.
- Copper metabolism. The authors say that KO of either PDZD11 or PLEKHA6/7 results in higher Cu levels. What does this mean in terms of physiology and pathology? In the context of Menkes disease one has to show that this intracellular Cu increase is due to a reduction in Cu release from the cells. So, Cu release from the cells into medium has to be measured by ICP-MS or Cu64. On the other hand, it would be important to understand whether Cu accumulation in KO cells is toxic. To this end viability of KO cells should be tested in Cu dose-response experiments.
- How critical is WW-PLEKHAs or PDZD11 deficiency in terms of Cu metabolism? Are there genetic disorders or mouse phenotypes associated with their loss of function? If yes, do these phenotypes include any impairment of Cu metabolism?
- Discussion. Could PH domains of WW-PLEKHAS be involved in their basolateral localization, thereby generating a targeting patch for ATP7A? Some publications suggest that the basolateral membrane might be enriched in specific PIPs, which in turn generates a favorable environment for some PH domains. Is this the case for PH domains of WW-PLEKHAS?
Minor points:
- Fig. 6C. CFP-HA is a negative control but still gives a band (although of lower intensity). So how can one be sure that other interactions are specific? This is particularly worrying because the quantification shows a very minor (less than 1.5) increase in the intensity of bands corresponding to specific interactors.
- Page 11. The result section title "WW-PLEKHAs promote PDZD11 binding to ATP7A through PDZD11 (Figure 6)" does not sound right and has to be corrected.
Significance
Delivery of copper transporter ATP7A to the basolateral surface of epithelial cells is of great importance for maintenance of copper metabolism and, hence for human health in general. Impairment of this process in enterocytes causes fatal Menkes disease. However, the mechanisms driving basolateral targeting of ATP7A remained poorly characterized. This study provides a significant advance in our understanding of these mechanisms and opens new avenues for investigation of how WW-PLEKHAs/PDZD11-mediated targeting of ATP7A might be affected in the context of inherited disorders of copper metabolism.
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Reply to the reviewers
Editor comments:
Thank you for sending your manuscript entitled "In situ imaging of bacterial membrane projections and associated protein complexes using electron cryo-tomography" to Review Commons. We have now completed the peer review of the manuscript. Please find the full set of reports below.
We thank the editors of Review Commons and all the reviewers for their insightful comments which helped us to improve our manuscript. We have now modified our manuscript based on the Reviewers’ comments and would like to ask you to consider our revised manuscript for publication.
Reviewer #1:
This manuscript by the Jensen lab surveys a plethora of bacterial outer-membrane projections captured over the years by in situ cryo-tomography under near-native conditions. The authors classify the different visualized structures, highlighting both similarities and differences among them. They further describe molecular complexes that are associated with these projections. The manuscript highlights the abundance of such understudied structures in nature, indicating the need to deepen our exploration into their biological functions and mechanisms of action.
We thank the reviewer for her/his insightful comments that allowed us to improve our manuscript.
The authors should state in the Abstract and Introduction that only diderm bacteria and outer- membrane extensions are included in the study.
Done. We have modified the title, the abstract and the introduction to explicitly highlight this point.
In the Introduction or Discussion the authors should mention the limits of the in situ cryo-tomography, such as the difficulty to observe regions in between neigbouring bacterial cells, and into the thick bacterial cell body.
Done. We have added the following to our revised manuscript:
“Currently, only electron cryo-tomography (cryo-ET) allows visualization of structures in a near-native state inside intact (frozen-hydrated) cells with macromolecular (~5 nm) resolution. However, this capability is limited to thin samples (few hundred nanometers thick, like individual bacterial cells of many species) while thicker samples like the central part of eukaryotic cells, thick bacterial cells, or clusters of bacterial cells are not amenable for direct cryo-ET imaging. Such thick samples can be rendered suitable for cryo-ET experiments by thinning them first using different methods including focused ion beam milling and cryosectioning [30]. Cryo-ET has already been invaluable in revealing the structures of several membrane extensions, including Shewanella oneidensis nanowires [6], Helicobacter pylori tubes [15], Delftia acidovorans nanopods [25], Vibrio vulnificus OMV chains [16], and more recently cell-cell bridges in the archaeon Haloferax volcanii [31].” (Lines 108-118)
Please provide a legend to Table S1 explaining the numbers (organelles?), how many cells were viewed? I think that at least part of it should be included in the main text. Also, there are examples of vesicles emanating from H. pylori. This information is missing from Table S1.
Done. We added a column to the table indicating the number of cells available for each species. We also added the information about the vesicles in H. pylori to the table. This table is now incorporated into the main text of the manuscript as Table 1.
Please provide an ordered list including all the strains (and IDs of the specific isolates) used in this study and their genotypes.
Done. We added Table S1 to the revised manuscript that contains this information. This table also includes relevant references to all the published papers where these strains were previously used.
The authors describe in detail the H. pylori tubes that seem to be flagellum-core independent. However, the authors found previously (ref 15) that during infection, these structures are dependent on CagA T4SS, and they visualized T4SS sub-complexes in proximity to the point of tube emanation. This should be described and discussed in the text. Also, please indicate if the "host-independent" tubes are similarly dependent on T4SS.
Done. We added the following to the revised manuscript:
“The scaffolded uniform tubes of H. pylori that we observed were formed in samples not incubated with eukaryotic cells, indicating that they can also form in their absence. However, the tubes we found had closed ends and no clear lateral ports, while some of the previously-reported tubes (formed in the presence of eukaryotic host cells) had open ends and prominent ports [15]. It is possible that such features are formed only when H. pylori are in the vicinity of host cells. Moreover, while it was previously hypothesized that the formation of membrane tubes in H. pylori (when they are in the vicinity of eukaryotic cells) is dependent on the cag T4SS [15], we could not identify any clear correlation between the emanation of membrane tubes and cag T4SS particles in our samples where H. pylori was not incubated with host cells. We also show that the tubes of H. pylori are CORE-independent, indicating that they are different from the CORE-dependent nanotubes described in other species.” (Lines 303-313)
Is there any difference in the frequency or length of the tubes in the mutants presented in Figure 4? The flgS mutant in the image exhibits a very short filament; is that typical?
We did not see any significant statistical difference in the number or lengths of the tubes in these different mutants. We added Table S2 to the revised manuscript which details the number of cells we visualized for each mutant and the number of the tubes seen there. In all these mutants the lengths of the tubes ranged between few tens to hundreds of nanometers. In addition, we added Fig. S2 to show more examples of these tubes in each of these mutants.
Minor points:
-Please check full bacterial names that are sometimes missing (e.g., lines 110-112).
Done.
-There is no reference to panel 2G. Please check the references to all panels.
Done. Please see lines 154 and 183 in the main text.
-Lines 181-184: There is no figure related to the formation of teardrop-like extensions from C. pinensis. Please review the text accordingly.
Done. Corrected.
-Line 235, not clear to what "as these" refers to.
Done. We modified the text as the following:
“As these MEs/MVs from S. oneidensis were purified” (Lines 246-247)
-Line 241, not clear what "a secretin-like complex" is, and no reference is provided.
Done. We modified the text as the following:
“In the third category, we observed a secretin-like complex in many tubes and vesicles of F. johnsoniae. Secretins are proteins that form a pore in the outer membrane and are associated with many secretion systems like type IV pili and type II secretion systems (T2SS) [39–41]” (Lines 252-254)
Reviewer #1 (Significance)
As described in this manuscript, even in model bacteria these structures are generated (e.g., Caulobacter forms the hardly studied nanopod extensions). The manuscript also provides visual categories of these structures, defining "extension types" that are likely to be used by the scientific community for years to come, similar to the initial pili classification during the 1960s-70s. It is a "descriptive study," in the positive sense of the term, as it significantly contributes to the field of bacteriology.
We thank the reviewer for her/his kind words and enthusiasm about our work. It is an honor to have our work compared to the seminal pili classification work done in the 1960s-70s by pioneers in the field of bacteriology.
Reviewer #2:
The manuscript "In situ imaging of bacterial membrane projections and associated protein complexes using electron cryo-tomography" by Kaplan et al., identifies and catalogues membrane extensions (MEs) and membrane vesicles (MVs) from 13 different species using cryo-electron tomography. Furthermore, they identify and discuss several protein complexes observed in these membrane projections.
The manuscript is beautifully written, interesting, and genuinely got this reviewer excited about the biology. I applaud the authors on their manuscript and have only minor comments and a few thoughts that the authors may wish to think on and discuss.
We thank the reviewer for her/his kind words and insightful comments that allowed us to improve our manuscript.
Some schematics throughout the introduction would be useful to readers new to the field/ outside the field who are not used to these different membrane structure features.
We thank the Reviewer for this suggestion. First, we made an extra figure with schematics showing the cell body and membrane tubes but that was rather redundant with Figure 8. For this reason, we added explicit labels to figure 1 highlighting the cell body and the tubes in these examples to help the reader following that figure and the subsequent ones. However, if the Reviewer has an explicit suggestion/view about the schematics then we would be very happy to do that.
The size of scale bars should be indicated on the figure panels themselves rather than in the figure legend to assist the reader.
Done.
In reference to lines 193-196 - what was the extracellular environment like in these micrographs? Were other cells present? Could it be the extracellular environment/surrounding cells that stimulate pearling? Have the authors considered this? Please discuss if relevant/insightful.
This is a good point. The cells were usually plunge-frozen in their standard growth media (except in H. pylori where the cells were resuspended in PBS and subsequently plunge-frozen). Yes, there are other cells present in the sample, however, usually, only one cell is present in the field of view of the tomogram as areas with multiple cells have thick ice and therefore not amenable for cryo-ET imaging. We added the following to the revised manuscript:
“As usually only one (or part of a) cell is present in the cryo-tomogram, we can’t exclude that differences in the extracellular environments, like the presence of a cluster of cells in the vicinity of the individual cells with pearling tubes, might play a role in this observation” (Lines 198-201).
"Randomly-located complexes" in this reviewers opinion should actually be described "seemingly randomly-located complexes" given there may be an organization present that is beyond the resolution limit of this study.
The is a good point. Indeed, we can’t exclude that these complexes have a preferred localization in specific lipid patches that we can’t detect in our cryo-tomograms. We added the following statement to the revised manuscript:
“These complexes, which were also found in the OM of intact cells, did not exhibit a preferred localization or regular arrangement within the tube at least within the fields of view provided by our cryo- tomograms (Fig. 5a & b).” (lines 227-230).
In reference to lines 287-292 - is it possible this has to do with lipid composition? Have the authors considered this? Please discuss if relevant/insightful.
Done. We added the following to the revised manuscript:
“In addition, differences in the lipid compositions among the various species investigated here might also play a role in the formation of these different forms of projections” (Lines 299-301).
Reviewer #2 (Significance ):
These results advance the field by shedding new light on bacterial membrane extension morphologies. The authors use a cryo-ET to catalogues membrane extensions and membrane vesicles which has not been done before.
This paper is likely to be of interest to structural biologists, biophysicist, membrane protein biologists, virologists and microbiologists.
This reviewer is a single-particle cryo-EM structural biologist with interest in membrane proteins._
We thank the reviewer for her/his enthusiasm about our work described here.
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Referee #2
Evidence, reproducibility and clarity
The manuscript "In situ imaging of bacterial membrane projections and associated protein complexes using electron cryo-tomography" by Kaplan et al., identifies and catalogues membrane extensions (MEs) and membrane vesicles (MVs) from 13 different species using cryo-electron tomography. Furthermore, they identify and discuss several protein complexes observed in these membrane projections.
The manuscript is beautifully written, interesting, and genuinely got this reviewer excited about the biology. I applaud the authors on their manuscript and have only minor comments and a few thoughts that the authors may wish to think on and discuss.
- Some schematics throughout the introduction would be useful to readers new to the field/ outside the field who are not used to these different membrane structure features.
- The size of scale bars should be indicated on the figure panels themselves rather than in the figure legend to assist the reader.
- In reference to lines 193-196 - what was the extracellular environment like in these micrographs? Were other cells present? Could it be the extracellular environment/surrounding cells that stimulate pearling? Have the authors considered this? Please discuss if relevant/insightful.
- "Randomly-located complexes" in this reviewers opinion should actually be described "seemingly randomly-located complexes" given there may be an organization present that is beyond the resolution limit of this study.
- In reference to lines 287-292 - is it possible this has to do with lipid composition? Have the authors considered this? Please discuss if relevant/insightful.
Significance
These results advance the field by shedding new light on bacterial membrane extension morphologies. The authors use a cryo-ET to catalogues membrane extensions and membrane vesicles which has not been done before.
This paper is likely to be of interest to structural biologists, biophysicist, membrane protein biologists, virologists and microbiologists.
This reviewer is a single-particle cryo-EM structural biologist with interest in membrane proteins.
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Referee #1
Evidence, reproducibility and clarity
This manuscript by the Jensen lab surveys a plethora of bacterial outer-membrane projections captured over the years by in situ cryo-tomography under near-native conditions. The authors classify the different visualized structures, highlighting both similarities and differences among them. They further describe molecular complexes that are associated with these projections. The manuscript highlights the abundance of such understudied structures in nature, indicating the need to deepen our exploration into their biological functions and mechanisms of action.
Comments:
- The authors should state in the Abstract and Introduction that only diderm bacteria and outer-membrane extensions are included in the study.
- In the Introduction or Discussion the authors should mention the limits of the in situ cryo-tomography, such as the difficulty to observe regions in between neigbouring bacterial cells, and into the thick bacterial cell body.
- Please provide a legend to Table S1 explaining the numbers (organelles?), how many cells were viewed? I think that at least part of it should be included in the main text. Also, there are examples of vesicles emanating from H. pylori. This information is missing from Table S1.
- Please provide an ordered list including all the strains (and IDs of the specific isolates) used in this study and their genotypes.
- The authors describe in detail the H. pylori tubes that seem to be flagellum-core independent. However, the authors found previously (ref 15) that during infection, these structures are dependent on CagA T4SS, and they visualized T4SS sub-complexes in proximity to the point of tube emanation. This should be described and discussed in the text. Also, please indicate if the "host-independent" tubes are similarly dependent on T4SS.
- Is there any difference in the frequency or length of the tubes in the mutants presented in Figure 4? The flgS mutant in the image exhibits a very short filament; is that typical?
Minor points:
- Please check full bacterial names that are sometimes missing (e.g., lines 110-112).
- There is no reference to panel 2G. Please check the references to all panels.
- Lines 181-184: There is no figure related to the formation of teardrop-like extensions from C. pinensis. Please review the text accordingly.
- Line 235, not clear to what "as these" refers to.
- Line 241, not clear what "a secretin-like complex" is, and no reference is provided.
Significance
As described in this manuscript, even in model bacteria these structures are generated (e.g., Caulobacter forms the hardly studied nanopod extensions). The manuscript also provides visual categories of these structures, defining "extension types" that are likely to be used by the scientific community for years to come, similar to the initial pili classification during the 1960s-70s. It is a "descriptive study," in the positive sense of the term, as it significantly contributes to the field of bacteriology.
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www.biorxiv.org www.biorxiv.org
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
In this manuscript, Mishima et al., designed a reporter system (dubbed PACE, for Parallel Analysis of Codon Effects) to assess the effect of codon usage in regulating mRNA stability in a controlled sequence context. This reporter corresponds to a stretch of 20 repetitions of a given codon (to be tested for its effect on mRNA stability), each repetition being separated by one codon corresponding to each of the 20 canonical amino acids. This stretch is inserted at the 3' end of the coding sequence of a superfolder GFP flanked with fixed 5' and 3' untranslated regions. In vitro transcribed capped and polyadenylated RNAs are then produced from these reporters (each with a specific stretch of repetitions of a given codon), pooled together and injected into zebrafish zygotes to monitor their relative abundance at different time points upon injection.
Using the PACE reporter, the authors were able to obtain a quantitative estimation of the impact of 58 out of the 61 sense codons on modulating mRNA stability. Their results are in agreement with a previous report that estimated the effect of codon usage on mRNA stability using endogenous mRNAs and an ORFeome library (Bazzini et al., 2016). However, contrary to relying on endogenous mRNAs and ORFeome reporters, the advantage of the PACE strategy is that the effect of the codon to be studied can be probed in a defined context, thus avoiding the presence of other motifs or transcript features that could also regulate mRNA stability. Similarly to results from Bazzini et al., 2016, the authors show that blocking translation completely abrogates the effect of codon usage, indicating that translation is required to drive codon-dependent mRNA degradation from their reporters. Also, the extent of codon-dependent mRNA decay is correlated with tRNA abundance and occurs through a process involving mRNA deadenylation as previously described in the zebrafish (Mishima et al., 2016 and Bazzini et al., 2016).
Having validated their PACE protocol, the authors performed ribosome profiling to test whether ribosome occupancy on tested codons is correlated with their capacity to drive mRNA degradation. Their results indicate that, at least for polar amino acids, there is indeed an inverse correlation between ribosome occupancy at tested codons and mRNA stability thus suggesting that slow decoding of codons due to low levels of available cognate tRNA can induce mRNA degradation. The authors further validate this finding by reducing the levels of aminoacylated tRNAAsn (corresponding a polar amino acid) and showing that stability of the reporter RNA carrying a stretch of AAC codons (decoded by tRNAAsnGUU) is reduced. To test whether codon-dependent mRNA degradation in the context of slow ribosome decoding lead to ribosome stalling and collisions, the authors generated a mutant zebrafish strain with impaired expression of ZNF598 (an essential factor of the No-Go decay (NGD) pathway in yeast). They also integrated a known ribosome stalling sequence from hCMV (and a mutant version that does not trigger ribosome stalling) in their sfGFP reporter construct as a positive control for NGD in their assays. Their results indicate that although ZNF598 depletion impairs degradation of the hCMV reporter (as expected), it does not affect codon-dependent mRNA degradation, which appears to occur for most codons through a NGD-independent manner. Finally, through the use of a tandem ORF reporter assay separated by codon tags to be tested, the authors show that destabilizing codons do not stall ribosomes but only lead to their transient slowdown which induces mRNA deadenylation and degradation in a ZNF598-independent manner.
Overall, the manuscript is very well written and pleasant to read. The introduction is well documented and relevant to the study as it allows readers to place the study in the current context of the field while highlighting open questions that have not been addressed yet. The results are clearly presented, the technical approaches are elegant and the conclusions convincing.
Below you will find some major and minor points that, in my opinion, should be addressed by the authors.
**Major point:**
- One interesting aspect of the PACE reporter assay is the possibility to monitor ribosome occupancy in parallel for all codon-tags tested, which the authors did in Figure 3. However, instead of using RNA-seq data to normalize ribosome footprints and obtain ribosome occupancy, the authors used an alternative normalization approach consisting, for each codon-tag, to calculate the number of ribosome footprints with test codons in the A site divided by the number of ribosome footprints with spacer codons in the A site. This approach is elegant and appears to work with codons corresponding to polar amino acids. However, it might have its limitations for other codons.
Indeed, ribosome dwell times (in yeast and mammals) have been shown to respond both to tRNA availability but also to other features such as the nature of the pair of adjacent codons, and the nature of the amino acid within the exit channel (Gobet C et al., 2020 PNAS; Gamble CE et al., 2016 Cell; Pavlov MY et al., 2009 PNAS). However, based on the work of "Buschauer R et al., 2020 Science", only ribosomes lacking an accommodated tRNA at the A site are able to recruit Ccr4-Not to mediate mRNA deadenylation and degradation. Other events that increase ribosome dwell time (and thus occupancy), such as slow peptidyl-transfer, do not lead to Ccr4-Not recruitment and are resolved by eIF5A. It is therefore possible that depending on the nature of the codon that is being tested, ribosome occupancy at test and spacer codons can be biased by the nature of codon-pairs and "dilute" the effects of tRNA availability.
If the authors performed RNA-seq together with the ribosome profiling experiment, it might be interesting to use the RNA-seq data to calculate ribosome occupancy on "tested" and "spacer" codons to check whether using this normalization, they do find a negative correlation between ribosome occupancy and PACE stability. A different approach would be to perform ribosome run-off experiments using harringtonine and estimate the elongation speed across the codon tag. However, I am aware that this experiment could be tedious an expensive.
- Figure 6: Insertion of the Lys x8 AAA stretch in the tandem ORF reporter leads to a decrease in HA-DsRedEx expression compared to that of Myc-EGFP. However, results from "Juszkiewicz and Hedge, 2017" using a similar reporter in mammalian cells indicate that stretches of Lys AAA below 20 repetitions only elicit poor RQC (less than 10% of true ribosome stalling for 12 repetitions of the AAA codon). Instead, most of the loss in RFP signal results from a change in the reading frame of ribosomes due to the "slippery" translation of the poly(A) stretch. I therefore think that it could be important to perform the experiment in ZNF598 KO embryos to validate that the observed reduction in HA-dsRedEx does indeed result from stalling and RQC and not from a change in the reading frame of ribosomes.
On a similar note, how do the authors explain the decrease in signal of the Flag-EGFP and HA-DsRedEx observed when using the Flag-EGFP with non-optimal codons? I understand that RQC occurring through NGD leads to ribosome disassembly at the stalling site and possibly mRNA cleavage (thus explaining the decrease in HA-DsRedEx signal compared to Myc-EGFP). However, I would assume that codon-mediated mRNA decay (even for ORF longer than 200 of non-optimal codons) should trigger mRNA deadenylation, followed by decapping and co-translational 5'to3' mRNA degradation, following the last translating ribosome. I would therefore expect not to see any change in the HA-DsRedEx/Myc-EGFP ratio even for the non-optimal Flag-EGFP reporter. Could the 200 non-optimal codons trigger some background RQC through NGD? Or could there be some ribosome drop-off? It might be interesting to test the optimal and non-optimal Flag-EGFP reporters in the ZNF598 KO background to check whether the observed decrease in the relative amount of HA-DsRedEx results from stalling-dependent RQC.
**Minor comments:**
The color-coded CSC results from "Bazzini et al., 2016" presented at the bottom of panel B in figure 2 are misleading because many codons (such as PheUUU, AsnAAU, TyrUAC...) are lacking information. I have the impression that the authors used the combined data from the rCSCI (obtained from the reporter RNAs) and CSC (obtained from endogenous transcripts) corresponding to Figure 1F from Bazzini et al., 2016. This data set excluded all codons that were not concordant between the endogenous and reporter CSCs (which are those that are lacking a color code in Figure 2B from this study). However, in the scatter-plot of PACE Vs CSC (from Supplemental Figure 1D of this study), the authors used the complete set of CSC values from Bazzini et al .,2016. Could the authors please use the complete set of CSC values from Bazzini et al., 2016 to color code codons in their Figure 2B?
Figure 4B. The charged tRNA measurements seem to have been done in a single biological replicate (there aren't any error bars in the chart). I understand that the procedure is tedious and requires a large amount of total RNA to begin with, but it would be preferable to perform it in three biological replicates.
Supplementary Figure 2B. I do not understand what the figure represents. The legend is quite cryptic and states that the panel corresponds to the information content of each reading frame. More information should be given so that readers can understand how to interpret de figure and extract periodicity information.
Reviewer #1 (Significance (Required)):
Since the seminal work from Jeff Coller's laboratory in 2015 (Presnyak et al., 2015 Cell) showing a global and major role for codon optimality in determining mRNA half-lives in yeast, the role of codon usage in modulating translation and stability of mRNAs has been widely studied in different organisms (including zebrafish and mammals). As stated by the authors in the introduction, most studies have relied on correlation analyses between codon usage and mRNA half-lives from endogenous transcripts or from ORF libraries with fixed 5'UTR and 3'UTRs. This approaches could suffer from the presence of transcript features that can participate in other mRNA degradation pathways, which could limit their use when performing further mechanistic studies.
The work by Mishima and collaborators presents an original reporter assay that allows to evaluate the role of codon usage on regulating mRNA stability in a defined context, thus avoiding the impact of confounding factors that could bias the measurement of mRNA stability. Results obtained using this reporter are in good agreement with previous reports from Zebrafish (Bazzini et al 2016., and Mishima et al., 2016). From this validated reporter approach, the authors further show that codon-dependent mRNA degradation is directly related to tRNA availability and (at least partially) to ribosome occupancy (two factors already suggested as being important for codon-mediated decay in zebrafish, although they were based on correlation analyses). Furthermore, the authors show that codon-mediated mRNA decay occurs during productive mRNA translation and that it is functionally distinct from RQC induced by ribosome stalling. As a consequence, codon-mediated mRNA degradation is independent from the RQC factor ZNF598 (which they also validate for the first time as an important RQC factor in zebrafish). This information is new within metazoans since only in yeast it has been clearly shown that codon-mediated mRNA decay is distinct from RQC induced by ribosome stalling and collisions.
Taken together, the reported findings will be of interest to the community working on mRNA metabolism and translation. It could also interest, more broadly, scientists working on translational selection and genome evolution.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
In this manuscript, Mishima et al aim to determine if the RNA-mediated decay determined by codon optimality is part of the ribosome quality control pathway, triggered by slowed codon decoding and ribosome stalling or it is an independent pathway.
To this end, the authors capitalize on their previous work to design a very elegant high-throughput reporter system that can analyze individually codon usage, ribosome occupancy and tRNA abundance. This reporter system, called PACE, is rigorously validated throughout the manuscript, because blocking translation with a morpholino blocking the AUG codon demonstrated that the effects no RNA stability are translation dependent.
When most of the available codons are tested using the PACE system, the authors recapitulate codon optimality profiles similar to the ones previously uncovered using transcriptome-wide approaches.
Thanks to the design of the reporter, which alternates repeats of a test codon with random codons, the authors can calculate how quickly a ribosome decodes the test codon on average. With this approach, the authors uncover a negative correlation between RNA stability and ribosome density on codons for polar amino acids and suggest that codon optimality is related to a slower decoding of the codons.
With the PACE reporter validated, the authors can interrogate the system to gain mechanistic insights of codon optimality. First, they test if RNA decay and deadenylation mediated by codon optimality is determined, in part, by the levels of aminoacylated tRNAs available. The authors use a very elegant approach, as they overexpress a bacterial enzyme (AnsB) in zebrafish that degrades asparagine, effectively reducing the levels of tRNA-Asn. The authors demonstrate that AnsB turns a previously optimal Asn codon, AAC, into a non-optimal one. This effect is translated into RNA destabilization and deadenylation, but this effect in not extended to other codons encoding amino acids not affected by Asn. These results provide a direct experimental validation of the previously published observation of tRNA levels and codon optimality.
Finally, the authors interrogate the relationship between the codon optimality pathways and the ribosome quality control pathways, that takes care of stalled ribosomes. The authors generate a zebrafish mutant of Znf598, a vertebrate homolog of the yeast protein in charge of resolving stalled ribosomes. Using a maternal-and-zygotic mutant, the authors demonstrate that in these mutant's codon optimality proceeds as usual but ribosome stalling is not resolved, providing evidence for first time that Znf598 is involved in ribosome quality control in vertebrates.
Altogether, this manuscript presents work that builds on the previous findings of the authors and other labs but it is a qualitative leap forward rather than a marginal increment, because the body of work in the current manuscript i) establishes a reporter to dissect the mechanisms of codon optimality, ii) demonstrates that ribosome slow-down but not stalling is part of the trigger of RNA decay mediated by codon optimality, iii) demonstrates that this pathway is independent of ribosome quality control pathway and finally iv) demonstrates that vertebrate Znf598 is involved in the RNA decay mediated by ribosome stalling.
Due to these novel findings, and the rigor of the experimental design, this manuscript should be accepted for publication. The authors should first address the following comments:
**Major comment:**
- The authors very elegantly demonstrate the impact of AnsB on the stability of the RNA reporter, and it is precisely the simplicity of the reporter that allows the authors to draw clear conclusions. Nevertheless, it would be interesting to determine if the reporter results in embryos injected with AnsB also translate to endogenous genes rich in AAC codons. The authors could perform a polyA-selected RNA-Seq in embryos treated with AnsB to determine if the transcripts rich in AAC codons are destabilized compared to wild-type, thus validating the reporter results in endogenous genes. **Minor comments:**
In figure 5J the authors plot the normalized codon tag levels of the PACE reporter run in the MZznf598 mutant. The authors color code the labels in the x-axis following the PACE results in wild-type (figure 2B). The authors should also plot the wild-type values to have a direct visual comparison of the results trend in both genotypes. The authors focus in the title on the role of Znf598 or the lack thereof in RNA decay induced by codon optimality. However, for the non-aficionados in codon-optimality, ZnF598 is an unknown protein and adds little information to the title. The authors should provide a more informative title, directly pinpointing that codon-optimality is independent of the ribosome quality control pathway.
Reviewer #2 (Significance (Required)):
This manuscript presents work that builds on the previous findings made by the authors and other laboratories but it is a qualitative leap forward rather than a marginal increment, because the body of work in the current manuscript i) establishes a reporter to dissect the mechanisms of codon optimality, ii) demonstrates that ribosome slow-down but not stalling is part of the trigger of RNA decay mediated by codon optimality, iii) demonstrates that this pathway is independent of ribosome quality control pathway and finally iv) demonstrates that vertebrate Znf598 is involved in the RNA decay mediated by ribosome stalling.
In addition to the conceptual findings, the authors establish a new high-throughput reporter system to evaluate the influence of codon optimality in RNA decay.
The work its done in zebrafish embryos, an in vivo model system where codon optimality has been extensively tested by the authors and others, following the stability of reporter and endogenous genes.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
Mishima et al. address a very timely topic of how the codon composition of the ORF and the associated translation elongation speed affect mRNA stability. Several studies have already shown a strong correlation between codon optimality and mRNA stability - meaning the more "optimal" the codons, the faster supposedly the elongation speed and the more stable the mRNA. Most of these studies were done by analyzing global expression data, with limited follow up, therefore being also impacted by other co-translational mRNA decay pathways and in addition these studies could also not test directly the effect of each single codon on mRNA stability. The authors took a systematic reporter-based assay approach, called PACE, which allowed them to test systematically the effect of codon composition on mRNA decay. By integrating also ribosome profiling data, the authors could nicely show that the speed of translation (measured by ribosome density) correlates with their determined mRNA stability effect of each codon and also the corresponding tRNA levels. However, interestingly this seems to be the case only for codons encoding polar amino acids, but not the ones that encode charged or non-polar amino acids. It will be very interesting to find out why that is? Finally, the authors address if some of the effects they see might be due to ribosome collisions and associated no go decay (NGD). For this they generated a Znf598 mutant by CRISPR-Cas9. Znf598 is the proposed homolog of Hel2, the protein in yeast that is essential for NGD. The authors go on to show that NGD is defective in this mutant, but that codon mediated decay, which is elongation dependent, is not to a large part not dependent on Znf598.
**All minor comments:**
- It is intriguing why only polar AAs show a tRNA amount specific effect in the ribosome footprint data. Some hypothesis/discussion about this could be expanded further in the discussion or results.
- On the same token some additional analysis might be helpful. For example, in Figure 2E, the authors group codons in weak, neutral and strong based on PACE measurements and then look at the tRNA expression range for each of the three groups. Could the authors do this also separately for the codons of polar, non-polar and charged amino acids? What do you see - still the same pattern as for all the codons or do again only polar amino acids show the trend?
- Can the authors elaborate on the development of their PACE system? Why is it designed the way it is? What parameters did they test? For example, why the 20 amino acids tail, did you you test shorter sequences of the amino acid, spacer repeats, etc?
- The next few questions are a bit more of a technical nature regarding the reporter construct used for PACE.
- Did all AA pairs (Codon of interest + spacer codon) behave the same in the footprint assay? Does the data have enough information and resolution for this?
- Was the order of the spacer codons always the same in all the constructs? Could the specific order, if it is consistent, have any unseen consequences (ie. interaction with the exit tunnel)? Did the authors test other orders?
- Are the spacer codons optimized?
- Are the codons affected in the NGD mutant the ones that are most different in the Bazzini data?
- The authors inject directly mRNA into the embryos, therefore avoiding that the reporter mRNA is ever in the nucleus. However, there could be nuclear events (e.g. loading of particular proteins) that might affect the fate of an mRNA in the cytosol, among these the translation efficiency and also stability. Maybe some comment in the discussion as to the effect of missing nuclear factors would be welcome. This is not a criticism; it would just be nice to hear the authors' thoughts on that.
- Page 6; final paragraph: "Finally, we compared the speed of the ribosome translating mRNA destabilizing codons to that of an aberrantly stalled ribosome." Not sure the authors did that actually. They tested the effect of ribosome slowing down on protein production and mRNA levels and compared that to stalling ribosomes, but did not compare the "speed" directly and I am not even sure what they mean by that in this context. Probably good to rephrase.
Page 7, upper half: ".....by taking the positional effect of codon-mediated decay into account (Mishima and Tomari, 2016)."
This is my limited knowledge of the literature, but I think you should mention what this positional effect is and not just cite a paper.
Very minor, but on page 8 when PACE is introduced, the authors show the different destabilizing effects of the three Ile codons. While that is ok, in the section before, when the authors tested their construct by qRT-PCR, they focused on the two Leu codons. I would also mention them here and do a direct comparison of the qRT-PCR results with the pooled PACE result for these two codons. Based on the figure the two codons seem to behave qualitatively like expected, but I am not sure how good the quantitative behavior matches. The AnsB experiment - the authors only mention data about one of the two Asn codons (AAC), but what about the second Asn codon (AAU) - do you also see an effect on that codon upon overexpression of AnsB as well? AAU is already a quite destabilizing codon and you might not see a further increase in destabilization, but it would be great to know if there was or not. Page 13, second paragraph: More out of interest, but it is quite intriguing that GCG turned into a destabilizing codon (opposite of what one would expect if NGD would play a bit a role). Any speculation why? Page 14, end of page and related to Figure 6C: AAU seems much more destabilizing than AAC. Therefore, I would have expected that the inserted sequence with the AAU codons would lead actually to downregulation of the mRNA and therefore the EGFP and DsRFP total protein signal relative to the construct with the AAC inserted in between, even if the ratio of EGFP/DsRed seems unchanged. However, based on the western blot in 6C the total protein levels seem very similar. Isn't that surprising? Although, AAU obviously allows translation to proceed it should still induce a stronger mRNA decay than AAC and therefore result in less total mRNA (and protein level as a consequence). Did the authors quantify the exact levels of the reporter proteins and mRNA and compared them between the two constructs? Page 15, last sentence: Somehow for me the word "transient" is a bit hard to grasp in this context. What do you mean by that - do you really mean "impermanent" or "lasting only for a short amount of time"? Don't you simply mean "weaker", "less strong"? Page 17, second sentence: I think the authors want to reference here Figure 2E and not Figure 2D.
Reviewer #3 (Significance (Required)):
All in all, I have to say that it was a real pleasure to read this manuscript. The authors were extremely thorough with their experiments and did nearly never overstate any of their conclusions. It is a very insightful story, which in my opinion will contribute greatly to the field of gene expression and posttranscriptional gene expression regulation in particular. The PACE assay, although a bit artificial, gave very clean results, which agree with the previous literature and could be very useful for future studies. Generating the Znf598 mutant and showing that the codon-dependent decay is independent from NGD is a great addition to this paper. Although it is a bit of a pity that we do not see more of a characterization of the Znf598 mutant in this paper, I do agree with the authors that this might take away a bit of the focus of this manuscript and that the mutant deserves actually its own story. I only have very minor comments/questions for the authors that they should be able to address easily. Finally, I can only repeat myself by saying: congrats on this great paper and I fully support publication.
-
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Referee #3
Evidence, reproducibility and clarity
Mishima et al. address a very timely topic of how the codon composition of the ORF and the associated translation elongation speed affect mRNA stability. Several studies have already shown a strong correlation between codon optimality and mRNA stability - meaning the more "optimal" the codons, the faster supposedly the elongation speed and the more stable the mRNA. Most of these studies were done by analyzing global expression data, with limited follow up, therefore being also impacted by other co-translational mRNA decay pathways and in addition these studies could also not test directly the effect of each single codon on mRNA stability. The authors took a systematic reporter-based assay approach, called PACE, which allowed them to test systematically the effect of codon composition on mRNA decay. By integrating also ribosome profiling data, the authors could nicely show that the speed of translation (measured by ribosome density) correlates with their determined mRNA stability effect of each codon and also the corresponding tRNA levels. However, interestingly this seems to be the case only for codons encoding polar amino acids, but not the ones that encode charged or non-polar amino acids. It will be very interesting to find out why that is? Finally, the authors address if some of the effects they see might be due to ribosome collisions and associated no go decay (NGD). For this they generated a Znf598 mutant by CRISPR-Cas9. Znf598 is the proposed homolog of Hel2, the protein in yeast that is essential for NGD. The authors go on to show that NGD is defective in this mutant, but that codon mediated decay, which is elongation dependent, is not to a large part not dependent on Znf598.
All minor comments:
- It is intriguing why only polar AAs show a tRNA amount specific effect in the ribosome footprint data. Some hypothesis/discussion about this could be expanded further in the discussion or results.
- On the same token some additional analysis might be helpful. For example, in Figure 2E, the authors group codons in weak, neutral and strong based on PACE measurements and then look at the tRNA expression range for each of the three groups. Could the authors do this also separately for the codons of polar, non-polar and charged amino acids? What do you see - still the same pattern as for all the codons or do again only polar amino acids show the trend?
- Can the authors elaborate on the development of their PACE system? Why is it designed the way it is? What parameters did they test? For example, why the 20 amino acids tail, did you you test shorter sequences of the amino acid, spacer repeats, etc?
- The next few questions are a bit more of a technical nature regarding the reporter construct used for PACE. a. Did all AA pairs (Codon of interest + spacer codon) behave the same in the footprint assay? Does the data have enough information and resolution for this? b. Was the order of the spacer codons always the same in all the constructs? Could the specific order, if it is consistent, have any unseen consequences (ie. interaction with the exit tunnel)? Did the authors test other orders? c. Are the spacer codons optimized?
- Are the codons affected in the NGD mutant the ones that are most different in the Bazzini data?
- The authors inject directly mRNA into the embryos, therefore avoiding that the reporter mRNA is ever in the nucleus. However, there could be nuclear events (e.g. loading of particular proteins) that might affect the fate of an mRNA in the cytosol, among these the translation efficiency and also stability. Maybe some comment in the discussion as to the effect of missing nuclear factors would be welcome. This is not a criticism; it would just be nice to hear the authors' thoughts on that.
- Page 6; final paragraph: "Finally, we compared the speed of the ribosome translating mRNA destabilizing codons to that of an aberrantly stalled ribosome." Not sure the authors did that actually. They tested the effect of ribosome slowing down on protein production and mRNA levels and compared that to stalling ribosomes, but did not compare the "speed" directly and I am not even sure what they mean by that in this context. Probably good to rephrase.
- Page 7, upper half: ".....by taking the positional effect of codon-mediated decay into account (Mishima and Tomari, 2016)." This is my limited knowledge of the literature, but I think you should mention what this positional effect is and not just cite a paper.
- Very minor, but on page 8 when PACE is introduced, the authors show the different destabilizing effects of the three Ile codons. While that is ok, in the section before, when the authors tested their construct by qRT-PCR, they focused on the two Leu codons. I would also mention them here and do a direct comparison of the qRT-PCR results with the pooled PACE result for these two codons. Based on the figure the two codons seem to behave qualitatively like expected, but I am not sure how good the quantitative behavior matches.
- The AnsB experiment - the authors only mention data about one of the two Asn codons (AAC), but what about the second Asn codon (AAU) - do you also see an effect on that codon upon overexpression of AnsB as well? AAU is already a quite destabilizing codon and you might not see a further increase in destabilization, but it would be great to know if there was or not.
- Page 13, second paragraph: More out of interest, but it is quite intriguing that GCG turned into a destabilizing codon (opposite of what one would expect if NGD would play a bit a role). Any speculation why?
- Page 14, end of page and related to Figure 6C: AAU seems much more destabilizing than AAC. Therefore, I would have expected that the inserted sequence with the AAU codons would lead actually to downregulation of the mRNA and therefore the EGFP and DsRFP total protein signal relative to the construct with the AAC inserted in between, even if the ratio of EGFP/DsRed seems unchanged. However, based on the western blot in 6C the total protein levels seem very similar. Isn't that surprising? Although, AAU obviously allows translation to proceed it should still induce a stronger mRNA decay than AAC and therefore result in less total mRNA (and protein level as a consequence). Did the authors quantify the exact levels of the reporter proteins and mRNA and compared them between the two constructs?
- Page 15, last sentence: Somehow for me the word "transient" is a bit hard to grasp in this context. What do you mean by that - do you really mean "impermanent" or "lasting only for a short amount of time"? Don't you simply mean "weaker", "less strong"?
- Page 17, second sentence: I think the authors want to reference here Figure 2E and not Figure 2D.
Significance
All in all, I have to say that it was a real pleasure to read this manuscript. The authors were extremely thorough with their experiments and did nearly never overstate any of their conclusions. It is a very insightful story, which in my opinion will contribute greatly to the field of gene expression and posttranscriptional gene expression regulation in particular. The PACE assay, although a bit artificial, gave very clean results, which agree with the previous literature and could be very useful for future studies. Generating the Znf598 mutant and showing that the codon-dependent decay is independent from NGD is a great addition to this paper. Although it is a bit of a pity that we do not see more of a characterization of the Znf598 mutant in this paper, I do agree with the authors that this might take away a bit of the focus of this manuscript and that the mutant deserves actually its own story. I only have very minor comments/questions for the authors that they should be able to address easily. Finally, I can only repeat myself by saying: congrats on this great paper and I fully support publication.
-
Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.
Learn more at Review Commons
Referee #2
Evidence, reproducibility and clarity
In this manuscript, Mishima et al aim to determine if the RNA-mediated decay determined by codon optimality is part of the ribosome quality control pathway, triggered by slowed codon decoding and ribosome stalling or it is an independent pathway.
To this end, the authors capitalize on their previous work to design a very elegant high-throughput reporter system that can analyze individually codon usage, ribosome occupancy and tRNA abundance. This reporter system, called PACE, is rigorously validated throughout the manuscript, because blocking translation with a morpholino blocking the AUG codon demonstrated that the effects no RNA stability are translation dependent.
When most of the available codons are tested using the PACE system, the authors recapitulate codon optimality profiles similar to the ones previously uncovered using transcriptome-wide approaches.
Thanks to the design of the reporter, which alternates repeats of a test codon with random codons, the authors can calculate how quickly a ribosome decodes the test codon on average. With this approach, the authors uncover a negative correlation between RNA stability and ribosome density on codons for polar amino acids and suggest that codon optimality is related to a slower decoding of the codons.
With the PACE reporter validated, the authors can interrogate the system to gain mechanistic insights of codon optimality. First, they test if RNA decay and deadenylation mediated by codon optimality is determined, in part, by the levels of aminoacylated tRNAs available. The authors use a very elegant approach, as they overexpress a bacterial enzyme (AnsB) in zebrafish that degrades asparagine, effectively reducing the levels of tRNA-Asn. The authors demonstrate that AnsB turns a previously optimal Asn codon, AAC, into a non-optimal one. This effect is translated into RNA destabilization and deadenylation, but this effect in not extended to other codons encoding amino acids not affected by Asn. These results provide a direct experimental validation of the previously published observation of tRNA levels and codon optimality.
Finally, the authors interrogate the relationship between the codon optimality pathways and the ribosome quality control pathways, that takes care of stalled ribosomes. The authors generate a zebrafish mutant of Znf598, a vertebrate homolog of the yeast protein in charge of resolving stalled ribosomes. Using a maternal-and-zygotic mutant, the authors demonstrate that in these mutant's codon optimality proceeds as usual but ribosome stalling is not resolved, providing evidence for first time that Znf598 is involved in ribosome quality control in vertebrates.
Altogether, this manuscript presents work that builds on the previous findings of the authors and other labs but it is a qualitative leap forward rather than a marginal increment, because the body of work in the current manuscript i) establishes a reporter to dissect the mechanisms of codon optimality, ii) demonstrates that ribosome slow-down but not stalling is part of the trigger of RNA decay mediated by codon optimality, iii) demonstrates that this pathway is independent of ribosome quality control pathway and finally iv) demonstrates that vertebrate Znf598 is involved in the RNA decay mediated by ribosome stalling.
Due to these novel findings, and the rigor of the experimental design, this manuscript should be accepted for publication. The authors should first address the following comments:
Major comment:
- The authors very elegantly demonstrate the impact of AnsB on the stability of the RNA reporter, and it is precisely the simplicity of the reporter that allows the authors to draw clear conclusions. Nevertheless, it would be interesting to determine if the reporter results in embryos injected with AnsB also translate to endogenous genes rich in AAC codons. The authors could perform a polyA-selected RNA-Seq in embryos treated with AnsB to determine if the transcripts rich in AAC codons are destabilized compared to wild-type, thus validating the reporter results in endogenous genes.
Minor comments:
- In figure 5J the authors plot the normalized codon tag levels of the PACE reporter run in the MZznf598 mutant. The authors color code the labels in the x-axis following the PACE results in wild-type (figure 2B). The authors should also plot the wild-type values to have a direct visual comparison of the results trend in both genotypes.
- The authors focus in the title on the role of Znf598 or the lack thereof in RNA decay induced by codon optimality. However, for the non-aficionados in codon-optimality, ZnF598 is an unknown protein and adds little information to the title. The authors should provide a more informative title, directly pinpointing that codon-optimality is independent of the ribosome quality control pathway.
Significance
This manuscript presents work that builds on the previous findings made by the authors and other laboratories but it is a qualitative leap forward rather than a marginal increment, because the body of work in the current manuscript i) establishes a reporter to dissect the mechanisms of codon optimality, ii) demonstrates that ribosome slow-down but not stalling is part of the trigger of RNA decay mediated by codon optimality, iii) demonstrates that this pathway is independent of ribosome quality control pathway and finally iv) demonstrates that vertebrate Znf598 is involved in the RNA decay mediated by ribosome stalling.
In addition to the conceptual findings, the authors establish a new high-throughput reporter system to evaluate the influence of codon optimality in RNA decay.
The work its done in zebrafish embryos, an in vivo model system where codon optimality has been extensively tested by the authors and others, following the stability of reporter and endogenous genes.
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Referee #1
Evidence, reproducibility and clarity
In this manuscript, Mishima et al., designed a reporter system (dubbed PACE, for Parallel Analysis of Codon Effects) to assess the effect of codon usage in regulating mRNA stability in a controlled sequence context. This reporter corresponds to a stretch of 20 repetitions of a given codon (to be tested for its effect on mRNA stability), each repetition being separated by one codon corresponding to each of the 20 canonical amino acids. This stretch is inserted at the 3' end of the coding sequence of a superfolder GFP flanked with fixed 5' and 3' untranslated regions. In vitro transcribed capped and polyadenylated RNAs are then produced from these reporters (each with a specific stretch of repetitions of a given codon), pooled together and injected into zebrafish zygotes to monitor their relative abundance at different time points upon injection.
Using the PACE reporter, the authors were able to obtain a quantitative estimation of the impact of 58 out of the 61 sense codons on modulating mRNA stability. Their results are in agreement with a previous report that estimated the effect of codon usage on mRNA stability using endogenous mRNAs and an ORFeome library (Bazzini et al., 2016). However, contrary to relying on endogenous mRNAs and ORFeome reporters, the advantage of the PACE strategy is that the effect of the codon to be studied can be probed in a defined context, thus avoiding the presence of other motifs or transcript features that could also regulate mRNA stability. Similarly to results from Bazzini et al., 2016, the authors show that blocking translation completely abrogates the effect of codon usage, indicating that translation is required to drive codon-dependent mRNA degradation from their reporters. Also, the extent of codon-dependent mRNA decay is correlated with tRNA abundance and occurs through a process involving mRNA deadenylation as previously described in the zebrafish (Mishima et al., 2016 and Bazzini et al., 2016). Having validated their PACE protocol, the authors performed ribosome profiling to test whether ribosome occupancy on tested codons is correlated with their capacity to drive mRNA degradation. Their results indicate that, at least for polar amino acids, there is indeed an inverse correlation between ribosome occupancy at tested codons and mRNA stability thus suggesting that slow decoding of codons due to low levels of available cognate tRNA can induce mRNA degradation. The authors further validate this finding by reducing the levels of aminoacylated tRNAAsn (corresponding a polar amino acid) and showing that stability of the reporter RNA carrying a stretch of AAC codons (decoded by tRNAAsnGUU) is reduced. To test whether codon-dependent mRNA degradation in the context of slow ribosome decoding lead to ribosome stalling and collisions, the authors generated a mutant zebrafish strain with impaired expression of ZNF598 (an essential factor of the No-Go decay (NGD) pathway in yeast). They also integrated a known ribosome stalling sequence from hCMV (and a mutant version that does not trigger ribosome stalling) in their sfGFP reporter construct as a positive control for NGD in their assays. Their results indicate that although ZNF598 depletion impairs degradation of the hCMV reporter (as expected), it does not affect codon-dependent mRNA degradation, which appears to occur for most codons through a NGD-independent manner. Finally, through the use of a tandem ORF reporter assay separated by codon tags to be tested, the authors show that destabilizing codons do not stall ribosomes but only lead to their transient slowdown which induces mRNA deadenylation and degradation in a ZNF598-independent manner.
Overall, the manuscript is very well written and pleasant to read. The introduction is well documented and relevant to the study as it allows readers to place the study in the current context of the field while highlighting open questions that have not been addressed yet. The results are clearly presented, the technical approaches are elegant and the conclusions convincing.
Below you will find some major and minor points that, in my opinion, should be addressed by the authors.
Major point:
- One interesting aspect of the PACE reporter assay is the possibility to monitor ribosome occupancy in parallel for all codon-tags tested, which the authors did in Figure 3. However, instead of using RNA-seq data to normalize ribosome footprints and obtain ribosome occupancy, the authors used an alternative normalization approach consisting, for each codon-tag, to calculate the number of ribosome footprints with test codons in the A site divided by the number of ribosome footprints with spacer codons in the A site. This approach is elegant and appears to work with codons corresponding to polar amino acids. However, it might have its limitations for other codons.
Indeed, ribosome dwell times (in yeast and mammals) have been shown to respond both to tRNA availability but also to other features such as the nature of the pair of adjacent codons, and the nature of the amino acid within the exit channel (Gobet C et al., 2020 PNAS; Gamble CE et al., 2016 Cell; Pavlov MY et al., 2009 PNAS). However, based on the work of "Buschauer R et al., 2020 Science", only ribosomes lacking an accommodated tRNA at the A site are able to recruit Ccr4-Not to mediate mRNA deadenylation and degradation. Other events that increase ribosome dwell time (and thus occupancy), such as slow peptidyl-transfer, do not lead to Ccr4-Not recruitment and are resolved by eIF5A. It is therefore possible that depending on the nature of the codon that is being tested, ribosome occupancy at test and spacer codons can be biased by the nature of codon-pairs and "dilute" the effects of tRNA availability.
If the authors performed RNA-seq together with the ribosome profiling experiment, it might be interesting to use the RNA-seq data to calculate ribosome occupancy on "tested" and "spacer" codons to check whether using this normalization, they do find a negative correlation between ribosome occupancy and PACE stability. A different approach would be to perform ribosome run-off experiments using harringtonine and estimate the elongation speed across the codon tag. However, I am aware that this experiment could be tedious an expensive.
- Figure 6: Insertion of the Lys x8 AAA stretch in the tandem ORF reporter leads to a decrease in HA-DsRedEx expression compared to that of Myc-EGFP. However, results from "Juszkiewicz and Hedge, 2017" using a similar reporter in mammalian cells indicate that stretches of Lys AAA below 20 repetitions only elicit poor RQC (less than 10% of true ribosome stalling for 12 repetitions of the AAA codon). Instead, most of the loss in RFP signal results from a change in the reading frame of ribosomes due to the "slippery" translation of the poly(A) stretch. I therefore think that it could be important to perform the experiment in ZNF598 KO embryos to validate that the observed reduction in HA-dsRedEx does indeed result from stalling and RQC and not from a change in the reading frame of ribosomes. On a similar note, how do the authors explain the decrease in signal of the Flag-EGFP and HA-DsRedEx observed when using the Flag-EGFP with non-optimal codons? I understand that RQC occurring through NGD leads to ribosome disassembly at the stalling site and possibly mRNA cleavage (thus explaining the decrease in HA-DsRedEx signal compared to Myc-EGFP). However, I would assume that codon-mediated mRNA decay (even for ORF longer than 200 of non-optimal codons) should trigger mRNA deadenylation, followed by decapping and co-translational 5'to3' mRNA degradation, following the last translating ribosome. I would therefore expect not to see any change in the HA-DsRedEx/Myc-EGFP ratio even for the non-optimal Flag-EGFP reporter. Could the 200 non-optimal codons trigger some background RQC through NGD? Or could there be some ribosome drop-off? It might be interesting to test the optimal and non-optimal Flag-EGFP reporters in the ZNF598 KO background to check whether the observed decrease in the relative amount of HA-DsRedEx results from stalling-dependent RQC.
Minor comments:
- The color-coded CSC results from "Bazzini et al., 2016" presented at the bottom of panel B in figure 2 are misleading because many codons (such as PheUUU, AsnAAU, TyrUAC...) are lacking information. I have the impression that the authors used the combined data from the rCSCI (obtained from the reporter RNAs) and CSC (obtained from endogenous transcripts) corresponding to Figure 1F from Bazzini et al., 2016. This data set excluded all codons that were not concordant between the endogenous and reporter CSCs (which are those that are lacking a color code in Figure 2B from this study). However, in the scatter-plot of PACE Vs CSC (from Supplemental Figure 1D of this study), the authors used the complete set of CSC values from Bazzini et al .,2016. Could the authors please use the complete set of CSC values from Bazzini et al., 2016 to color code codons in their Figure 2B?
- Figure 4B. The charged tRNA measurements seem to have been done in a single biological replicate (there aren't any error bars in the chart). I understand that the procedure is tedious and requires a large amount of total RNA to begin with, but it would be preferable to perform it in three biological replicates.
- Supplementary Figure 2B. I do not understand what the figure represents. The legend is quite cryptic and states that the panel corresponds to the information content of each reading frame. More information should be given so that readers can understand how to interpret de figure and extract periodicity information.
Significance
Since the seminal work from Jeff Coller's laboratory in 2015 (Presnyak et al., 2015 Cell) showing a global and major role for codon optimality in determining mRNA half-lives in yeast, the role of codon usage in modulating translation and stability of mRNAs has been widely studied in different organisms (including zebrafish and mammals). As stated by the authors in the introduction, most studies have relied on correlation analyses between codon usage and mRNA half-lives from endogenous transcripts or from ORF libraries with fixed 5'UTR and 3'UTRs. This approaches could suffer from the presence of transcript features that can participate in other mRNA degradation pathways, which could limit their use when performing further mechanistic studies.
The work by Mishima and collaborators presents an original reporter assay that allows to evaluate the role of codon usage on regulating mRNA stability in a defined context, thus avoiding the impact of confounding factors that could bias the measurement of mRNA stability. Results obtained using this reporter are in good agreement with previous reports from Zebrafish (Bazzini et al 2016., and Mishima et al., 2016). From this validated reporter approach, the authors further show that codon-dependent mRNA degradation is directly related to tRNA availability and (at least partially) to ribosome occupancy (two factors already suggested as being important for codon-mediated decay in zebrafish, although they were based on correlation analyses). Furthermore, the authors show that codon-mediated mRNA decay occurs during productive mRNA translation and that it is functionally distinct from RQC induced by ribosome stalling. As a consequence, codon-mediated mRNA degradation is independent from the RQC factor ZNF598 (which they also validate for the first time as an important RQC factor in zebrafish). This information is new within metazoans since only in yeast it has been clearly shown that codon-mediated mRNA decay is distinct from RQC induced by ribosome stalling and collisions.
Taken together, the reported findings will be of interest to the community working on mRNA metabolism and translation. It could also interest, more broadly, scientists working on translational selection and genome evolution.
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Reply to the reviewers
We thank the reviewers for their thoughtful comments. We were delighted the reviewers found our results “compelling”, “striking”, “well presented”, “implications exciting”, “excellent results! really nice!”, “this microscopy is beautiful!” and “translational-dependence (of mRNA localization) in a transcript-specific way without perturbing translation globally”, which is a “complete surprise, and opens exciting doors to investigate how translation leads to mRNA organization and its connection to **tissue development” and “may represent a new pathway of mRNA transport”.
We also appreciated the comments regarding the “wide appeal”, “broad readership of readers”, and “broad interest” the reviewers gave to our manuscript regarding its impact, and also the comments of “well-written (and) well-cited”.
We can address all the concerns raised by the reviewers. In addition to textual changes, we will add the following to the Results section:
- Additional quantitation of smFISH beyond Figure 2;
- Addition of a negative (uniformly distributed) mRNA control and its quantitation;
- Western blots for our ΔATG lines to determine what and how much protein is made.
- Unbiased nuclear masking. Our specific responses are shown below, in blue.
Reviewer #1
**Major comments**
Fig. 1: Main and supplementary figures present smFISH signals for eight localized mRNAs, while in the results section authors describe that they analyzed twenty-five transcripts. Authors should explain the choice of transcripts presented in the paper.
We will include a panel in Fig. S1E to show every mRNA that we tested, and we will edit Table 1 to describe the observed subcellular localization.
We will edit the text, adding a few sentences to clarify, along the lines of: “O**ur survey revealed mRNAs with varying degrees of localization within epithelia that we divided into three classes: CeAJ/membrane localized, perinuclearly localized, and unlocalized (Fig. 1 and S1 and Table 1).” and “The rest of our tested mRNAs did not possess any evident subcellular localization at any of the analyzed embryonic stages/tissues and were not further investigated (Fig. S1E and Table 1).”
Moreover, smFISH signal of different localized mRNAs in epidermal cells was visualized at different stages (bean, comma or late comma), and authors did not comment what was the reason of such conditions. This may make transcripts localization results difficult to interpret, as further analysis showed that mRNA localization varied in a stage-specific manner.
We have clarified this point now in Figure legend 1: “Specific embryonic stages were selected for each transcript based on the highest degree of mRNA localization they exhibited.”
Did author used smFISH probes designed against endogenous mRNAs for all tested transcripts?
We did not. We clarify this point now in Materials and methods: “All probes were designed against the endogenous mRNA sequences except dlg-1 (some constructs), pkc-3, hmp-2, spc-1, let-805, and vab-10a, whose mRNA were detected with gfp probes in their corresponding transgenic lines (Table S2). An exception to this is Fig. S1A where we used probes against the endogenous dlg-1 mRNA.”.
Marking dlg-1 mRNA as dlg-1-gfp suggests that smFISH probe was specific for gfp transcript. Is it true? If yes, authors should compare localization of wild-type endogenous dlg-1 mRNA with that of the transcript encoding a fusion protein, to confirm that fusion does not affect mRNA localization.
Yes, in Fig. 1C we show smFISH for GFP (i.e., the tagged dlg-1 only). In Fig. S1A, we show smFISH against endogenous dlg-1. Tagged and endogenous dlg-1 mRNAs are both localized. We clarified this point in the main text: “Five of these transcripts were enriched at specific loci at or near the cell membrane: laterally and at the CeAJ for dlg-1 (Fig. 1C for endogenous/GFP CRISPR-tagged dlg-1::gfp mRNA and S1A for endogenous/non-tagged dlg-1 mRNA), (…)”. And in the Supplemental figure legend (Fig. S1A): “Endogenous/non-tagged dlg-1 mRNA shows CeAJ/membrane localization like its endogenous/GFP CRISPR-tagged counterpart.”
Fig. 2B: Authors conclude that at later stages of pharyngeal morphogenesis mRNA enrichment at the CeAJ decreased gradually in comparison to comma stage. Data do not show statistically significant decrease in ratio of localized mRNAs - for dlg-1: bean: 0.39{plus minus}0.09, comma: 0.29{plus minus}0.08, 1.5-fold: 0.30{plus minus}0.09; for ajm-1: bean: 0.36{plus minus}0.08, comma: 0.30{plus minus}0.05, 1.5-fold: 0.28{plus minus}0.09.
t-test (one-tailed) analysis revealed a significant difference between bean and comma stages for both dlg-1 and ajm-1 mRNAs. Statistical analysis and data will be provided.
Fig. 4: What was the difference between the first and the second __ΔATG transgenic line? Authors should analyze the size of the truncated DLG-1 protein that is expressed from the second Δ__ATG transgenic line that localizes to CeAJ. Knowing alternative ATGs and protein size may suggest domain composition of the truncated protein. This will allow to confront truncated protein localization with the results from.
We will perform a Western blot to determine the size and levels of proteins produced.
Fig. 5. Moreover, to prove that the localization of dlg-1 mRNA at the CeAJ is translation-dependent, additional experiment should be performed where transcripts localization will be analyzed in embryos treated with translation inhibitors such as cycloheximide (translation elongation inhibitor) and puromycin (that induces premature termination).
We believe this comment might refer to Fig. 4. If this is the case: drugs like cycloheximide and puromycin affect the translation of the whole transcriptome, whereas with our ΔATG experiment, we aimed to target the translation of one specific transcript and avoid secondary effects. Nevertheless, we understand Reviewer #1’s concern and will include a second experiment. In our hands, cycloheximide and puromycin have never worked in older embryos (it’s hard to get past the eggshell and into the embryo). Instead, we will use stress conditions, which induce a “ribosome drop-off” (Spriggs et al., 2010). Heat stress has been shown to decrease polysome occupancy (Arnold et al., 2014). We, therefore, have used heat-shock at 33°C for 30’, and the results are now shown in Fig. S4. These show the loss of RNA localization upon heat shock.
**Minor comments**
In the introduction section authors should emphasize the main goal and scientific significance of the paper.
We added this sentence to state the significance before summarizing the results: “To investigate the impact of mRNA localization during embryonic development, we conducted a single molecule fluorescence in situ hybridization (smFISH)-based survey (…)” and “Our data demonstrate that the dlg-1 UTRs are dispensable, whereas translation is required for localization, therefore providing an example of a translation-dependent mechanism for mRNA delivery in C. elegans.” To state the significance.
Fig 1A: It's hard to distinguish different colors on the schematics. Schematics presents intermediate filaments that are not included in the Table 1.
We modified Table 1 based on this and other reviewers’ comments.
Fig. 1C: dlg-1 transcript is marked as dlg-1-gfp on the left panel and dlg-1 on the right panel.
Corrected.
Fig. 2B: Axis labels and titles are not visible, larger font size should be used.
We will modify the graph (following Reviewer #2’s suggestion) and axes label and title sizes will be taken into account.
Fig. 5C: Enlarge the font size.
Will do.
Fig. S2: Embryonic stages should be marked on the figure for easier interpretation.
Added.
Reviewer #2
Major comments
Figure 2 requires a negative (or uniformly distributed) mRNA control for comparison. Figure 2C should be quantified. The plot quality should be improved, and appropriate statistical tests should be employed to strengthen the claimed findings.
We will add a negative control (jac-1 mRNA), and quantify Fig. 2C as well. Plots will be changed accordingly to the suggestion.
Most claims of perinuclear mRNA localization are difficult to see and not well supported visually or statistically. The usage of DAPI markers, membrane markers, 3D rendering, or a quantified metric would bolster this claim. Also, sax-7 is claimed to be perinuclear and elsewhere claimed to be uniform then used as a uniform control. Please explain or resolve these discrepancies more clearly.__
Regarding perinuclear mRNAs:
We are not trying to make a big statement out of these data as perinuclear (ER) localization of mRNAs coding for transmembrane/secreted proteins is well known. The aim of our study was to describe transcript localized at or in the proximity of the junction. However, we thought it was worth mentioning these examples of perinuclearly localized mRNAs (hmr-1, sax-7, and eat-20) for two reasons: scientific correctness – show accessory results that might be interesting for other scientists – and use as positive controls for our smFISH survey – these mRNAs were expected to localize perinuclearly for the reasons mentioned above. We will rewrite the text to make these points clearer.
Regarding sax-7 mRNA:
sax-7 mRNA localizes perinuclearly in sporadic instances (Fig S1C), but it is predominantly scattered throughout the cytoplasm (i.e., unlocalized). It presumably localizes perinuclearly in a translation-dependent manner as sax-7 codes for a transmembrane protein that would be targeted to the ER. We have described this ER-type of localization in the introduction and reiterated it partially in the first paragraph of the results. sax-7 UTRs are therefore presumably not responsible for subcellular localization, which would instead depend on a signal sequence. We will better clarify this point in the main text.
The major concern about the paper is the data display and interpretation of Figure 5C. I'm not comfortable with the approach the authors took of blurring out the nucleus. A more faithful practice would be to use an automated mask over DAPI staining or to quantify the entirety of the cell. If the entirety of the cell were quantified, one could still focus analysis on specific regions of relevance. The interpretations distinguishing membrane versus cytoplasmic localization (or mislocalization) are hard to differentiate in these images especially since they are lacking a membrane marker. The ability to make these distinctions forms the basis of Tocchini et al's two pathways of dlg-1 mRNA localization. These interpretations also heavily rely on how the image was processed through the different Z-stacks, and it's not clear to me how that was done. For example, the diffusion of mRNA in figure 5F and 5I are indistinguishable to my eye but are claimed to be different.
In the images, the nuclei have been blurred to allow the reader to focus on the cytoplasmic signal and not on the nuclear (transcriptional) signal as it is not meaningful for this study. In the quantitation, the nuclear signal has been unbiasedly and specifically removed from the analysis by cropping out the DNA signal from the other channels. The frontal plane views of the seam cells in Fig. 5 show maximum intensity projections (MIPs) of 3 Z-stacks (0.54 µm total) that each contain nuclei and, therefore, the transcriptional signal (schematics in Fig. 5B). We will clarify these points in the text.
Regarding cytoplasmic versus membrane-associated mRNAs, although we did not have a membrane marker, we relied on the brightness of the DLG-1::GFP signal to identify the cell borders (i.e., membranes) after over-exposure. This approach allowed us to discern apicobasal and apical sides for the intensity profile analyses. We will clarify this point as well in the text and, in parallel, we will try a different approach using transverse sections on top views to clarify our data.
To my eye, it seems that Figure 5 could be more faithfully interpreted to state that DGL-1 protein localization depends on the L27-SH3 domains. The Huk/Guk domains are dispensable for DLG-1 protein localization; however, through other studies, we know they are important for viability. In contrast, dlg-1 mRNA localization requires all domains of the protein (L27-Guk). It is exceptionally interesting to find a mutant condition in which the mRNA and protein localizations are uncoupled. It would be very interesting to explore in the discussion or by other means what the purpose of localized translation may be. Because, in this instance, proper mRNA localization and protein function are closely associated, it may suggest that DLG-1 needs to be translated locally to function properly.
We will rewrite the Results and Discussion to clarify our model. We agree that L27 and SH3 domains are critical, but we also detected effects of the HooK/GuK domains. We have refined our model to describe functions of the N and C termini for membrane or junctional localization.
The manuscript requires an improve materials & methods description of the quantification __procedures and statistics employed.__
We will add these points.
Minor & Major comments together - text
Summary statement: Is "adherent junction" supposed to be "adherens junction?"
Corrected.
Abstract: Sentence 1, I think they should add a caveat word to this sentence. Something like "...phenomenon that can facilitate sub-cellular protein targeting." In most instances this isn't very well characterized or known.
Corrected.
In the first paragraph, it might be good to mention that Moor et al also showed that mRNA localize to different regions to alter their level of translation (to concentrate them in high ribosome dense regions of the cell).
Added as follows: “For example, a global analysis of localized mRNAs in murine intestinal epithelia found that 30% of highly expressed transcripts were polarized and that their localization coincided with highly abundant regions in ribosomes **(Moor, 2017).”
There are some new studies of translation-dependent mRNA localization - that might be good to highlight - Li et al., Cell Reports (PMID: 33951426) 2021; Sepulveda et al., 2018 (PCM), Hirashima et al., 2018; Safieddine, et al 2021. Also, Hughes and Simmonds, 2019 reviews membrane associated mRNA localization in Drosophila. And a new review by Das et al (Nat Rev MCB) 2021 is also nice.
We will add them to the text.
Parker et al. did not show that the 3'UTR was dispensable for mRNA localization. They showed the 3'UTR was sufficient for mRNA localization.
Quoting from the paper Parker et al.: “3′UTRs of erm-1 and imb-2 were not sufficient to drive mRNA subcellular localization. Endogenous erm-1 and imb-2 mRNAs localize to the cell or nuclear peripheries, respectively, but mNeonGreen mRNA appended with erm-1 or imb-2 3′UTRs failed to recapitulate those patterns (Fig. 4A-D).” We will make this point clearer in the rewritten text.
In the second paragraph, the sentence about bean stages is missing one closing parenthesis.
Corrected.
Last paragraph: FISH is fluorescence, not fluorescent.
Corrected.
Both "subcellular" and "sub-cellular" are used.
Corrected.
Minor comments – Figures
Figure 1
o Figure 1A is confusing. It's not totally clear what the rectangles and circles signify. There are many acronyms within the figure. Which of the cell types depicted in the figure are shown here? For example, for the dorsal cells, which is the apical v. basal side?
We tried to simplify the cartoon for a general C. elegans epithelial cell. We followed schematics already shown in previous publications to maintain consistency. Acronyms and color-codes are listed in the corresponding figure legend and have been better clarified.
o Some of the colors are difficult to distinguish, particularly when printed out or for red/green colorblind readers. Is erm-1 meant to be a cytoskeletal associated or a basolateral polarity factor?
We understand the issue, but unfortunately, with 8 classes of factors, shades of gray might not solve the problem. We tried to circumvent the red-green issue changing red to dark grey. Furthermore, we added details about shapes to the figure legends. We will work to make the colors work better.
ERM-1 is a cytoskeletal-associated factor.
o The nomenclature for dlg-1 is inconsistent within "C".
Corrected.
o Please specify what the "cr" is in "cr.dlg-1:-gfp" in the legend.
Added.
Figure 2
o Can Figure 2C be quantified in a similar manner to 2A/2B?
Currently our script cannot do that, but we will try to optimize it to be able to quantify this type of images.
o 2B - please jitter the dots to better visualize them when they land on top of one another
Yes, we will.
o Please include a negative control example, a transcript that is not peripherally localized for comparison.
Yes, we will.
o There is no place in the text of the document where Fig 2C is referenced
Corrected (it was wrongly referred to as “2B”).
o I can't see any discernable ajm-1 localization in Fig 2A.
We added some arrowheads to point at specific examples and increased the intensities of the corresponding smFISH signal for better visualization.
o I can't see any dlg-1 pharyngeal localization in Fig2C.
We added some arrowheads to point at specific examples and increased the intensities of the corresponding smFISH signal for better visualization.
o More details on how the quantification was performed would be welcome. Particularly, in 2B, what is the distance from the membrane in which transcripts were called as membrane-associated? What statistics were used to test differences between groups?
We will add a full description of the script used as well as the statistic details.
Figure 3
o Totally optional but might be nice: can you make a better attempt to approximate the scale of the cartoon depiction?
The UTRs, especially the 5’ one, are much smaller than the dlg-1 gene sequence. A proper scaling of the cartoon to the actual sequences, would draw the attention away from the main subjects of this figure, the UTRs. Nevertheless, we made sure it is clear in the corresponding figure legend that the cartoon is not in scale: “The schematics are not in scale with the actual size of the corresponding sequences. UTR lengths: dlg-1 5’UTR: 61 nucleotides; sax-7 5’UTR: 63 nucleotides; dlg-1 3’UTR: 815 nucleotides; unc-54 3’UTR: 280 nucleotides.”
o The GFP as an asterisk illustration may be confusing for some readers. Could you add another rectangular box to depict the gfp coding sequence?
Corrected.
o This microscopy is beautiful!
Thanks Reviewer #2!
o Were introns removed? Is the endogenous copy still present?
All the transgenes were analyzed in a wild-type background, therefore, yes, the endogenous copy was still present. All the transgenes possessed introns. We will change the corresponding text as follows: “To test whether the localization of one of the identified localized mRNAs, dlg-1, relied on zip codes, we generated extrachromosomal transgenic lines carrying a dlg-1 gene whose sequence was fused to an in-frame GFP and to exogenous UTRs.”. In the figure “dlg-1 ORF” has been replaced with “dlg-1 gene”.
o The wording in the legend "CRISPR or transgenic" may be confusing as Cas9 genome editing is still a form of transgenesis.
We added “extrachromosomal” to clarify the nature of the mRNA.
o The authors state that the 5'-3'UTR construct produces perinuclear dlg-1 transcripts but in the absence of DAPI imaging, it's not clear that this is the case.
We could not find such a statement, but we tried to clarify the localization of these mRNAs in the text: “The mRNA localization patterns of the two UTR reporters were compared to the localization of dlg-1 transcripts from the CRISPR line (“wild-type”, Fig. 3A; Heppert et al., 2018), described in Fig. 2. Both reporter strains showed enrichment at the CeAJ and localization dynamics of their transcripts that were comparable to the wild-type cr.dlg-1 (Fig. 3B). These results indicate that the UTR sequences of dlg-1** mRNA are not required for its localization.”
o Which probe set was used? The gfp probe?
Yes, please see the main text: “Given that the transgenic constructs were expressed in a wild-type background, smFISH experiments were conducted with probes against GFP RNA sequences to focus on the transgenic dlg-1::GFP mRNAs (cr.dlg-1 and tg.dlg-1).”
o Here, sax-7 is used as a uniform control, but sax-7 is claimed in Fig S1B-D as being perinuclear. This is a bit confusing.
sax-7 mRNA localizes perinuclearly in sporadic instances (Fig S1C), but it is predominantly scattered throughout the cytoplasm (i.e., unlocalized). It presumably localizes perinuclearly in a translation-dependent manner as sax-7 codes for a transmembrane protein that would be targeted to the ER. We have described this ER-type of localization in the introduction and reiterated it partially in the first paragraph of the results. sax-7 UTRs are therefore presumably not responsible for any subcellular localization, which would instead rely on a signal sequence. We will better clarify this point in the main text.
Figure 4
o Excellent results! Really nice!
Thanks Reviewer #2!
o Fig 4A. The GFP depicted as a circle is strange.
We changed it into a rectangle.
o Fig 4A. Can you include the gene/protein name for easy skimming?
Added.
o Fig 4B. the color here is too faint and it is unclear what is being depicted. Overall, this part of the figure could be improved.
We are optimizing the coloring and simplifying the schematics.
o Were the introns removed?
No, the introns were maintained in this and in all our transgenic lines. We described our transgenic lines in the materials and methods section (now with more detail). What we depict in the scheme (Fig. 4A) is the mature RNA (now specified in the figure), therefore no introns depicted. We will also specify this in the main text.
Figure 5
o Fig 5A. can you add the gene/protein name
Added.
o Fig 5B. Can you make the example apicobasal (non-apical) mRNA more distinctive? If it had its own peak in the lower trace, the reader would more clearly understand that this mRNA will be excluded from apical measurements whereas it will be included in apicobasal measurements.
We actually wanted to show this specific example: a cytoplasmic mRNA and a junctional mRNA may seem close from the apicobasal analysis (partially overlapping peaks that Reviewer #2 mentioned). With the apical analysis, instead, we can show that these mRNAs are actually not close, and they belong to two different compartments (cytoplasm and junction). We would therefore like to keep the current scheme, while better clarifying this point in the corresponding figure legend.
o D' - I' The grey font is too light.
Noted. We will change it.
o D' - I' The inconsistent y-axis scaling makes it difficult to compare across these samples. Can you set them to the same maximum number?
The values are indeed quite different. We tried to use the same scale, but this would make some of the data unappreciable. The idea was to evaluate, within each graph, how mRNA and protein are localized relative to the junctional marker. We will make this clearer in the text.
o D' - I' The x-axis labels are formatted incorrectly
Corrected.
o The practice of masking out the nucleus appears to remove potentially important mRNAs that are not nuclear localized. This could really impact the findings and interpretation. Instead, consider an automated DAPI mask.
The masking on the images is not the same used for the analysis: in the images, a shaded circle has been drawn on the DNA channel and moved onto its corresponding location in the other channels or merges. For the analysis, the DNA signal has been specifically removed in the channel with the smFISH signal. Given that the analysis has been performed on maximum intensity projections of 3 Z-stacks, we believe we did not remove any non-nuclear mRNA. We will clarify this point in Materials and methods.
o I can't see what the authors are calling membrane diffuse versus cytoplasmic. This is making it hard for me to see their "two step" pathway to localization.
We will add in Fig. 5B-C an example of a membrane localized mRNA. Furthermore, we will add transverse sections of membrane and cytoplasm to make the date clearer to the reader.
o Can more details of the quantification be included? How were Z-sections selected, chosen for inclusion? Which Z-sections and how many were selected?
We will add the details to Materials and methods.
o Also, why do these measurements focus on what I think are the seam cells when Lockwood et al., 2008 show the entire epithelium that is much easier to see?
We are focusing on the seam cells at the bean stage as these are the cells and the embryonic stage where we see the highest localization of dlg-1 mRNA in the wild-type.
o Please name these constructs to correlate the text more explicitly to the figures.
Added.
o How many embryos were analyzed for each trace? How many embryos showed consistent patterns?
We will add the details of the analysis to Materials and methods.
o Why were these cells used for study here? Lockwood et al., 2008 use a larger field of epithelial cells for visualization.
As stated before: we are focusing on the seam cells at the bean stage as these are the cells and the embryonic stage where we see the highest localization of dlg-1 mRNA in the wild-type.
Figure 6
There are major discrepancies between what this figure is depicting graphically and what is described in the text. Again, I'm not comfortable making the "two step" claims this figure purports given the data shared in Figure 5.
We are planning to re-write the last part of the results to better clarify our two-step model. A two-step model had been previously suggested in McMahon et al., 2001, where they could show that DLG-1 and AJM-1 (referred to in that publication as JAM-1) are initially localized laterally and only later in development are then enriched apically. Our data agree with McMahon very well, so we used the earlier study as a start. We will cite and explain this paper in greater depth during the rewriting.
**Minor comments - Tables & Supplemental Figures**
Table 1
I think this table could be improved to more clearly illustrate which mRNAs were tested and what their mRNA localization patterns were (for example, gene name identifiers included, etc). Could the information that is depicted by gray shading instead be added as its own column? For example, have a column for "Observed mRNA localization"
We modified Table 1 based on these and the other reviewers’ comments.
Can you add distinct column names for the two columns that are labeled as "protein localization - group"
We modified Table 1 based on these and the other reviewers’ comments.
Can you also add which of these components are part of ASI v. ASII (as described in the introduction?)
A new table has been added with the factors belonging to the two adhesion systems (same color code as in Table 1).
Supplemental Figure 1
It is hard to see that some of these spots are perinuclear. More information (membrane marker, 3D rendering, improved metrics) is required to support this claim.
We are not trying to make a big statement out of these data as perinuclear localization for mRNAs coding for transmembrane/secreted proteins is well known. The aim of our study was to describe transcript localized at or in the proximity of the junction. We thought it was worth mentioning these examples of perinuclearly localized mRNAs (hmr-1, sax-7, and eat-20) for two reasons: scientific correctness – show accessory results that might be interesting for other scientists – and use as positive controls for our smFISH survey – these mRNAs were expected to have a somewhat perinuclear localization for the reasons mentioned above.
What do these images look like over the entire embryo, not just in the zoomed in section?
We added a column with the zoom-out embryos.
sax-7 localization in S4 looks similar but a different localization claim is made.
sax-7 mRNA can localize perinuclearly in sporadic instances (Fig S1C), but is predominantly scattered throughout the cytoplasm (i.e., unlocalized). It presumably localizes perinuclearly in a translation-dependent manner as sax-7 codes for a transmembrane protein that would be targeted to the ER. We have described this ER-type of localization in the introduction and reiterated it partially in the first paragraph of the results. sax-7 UTRs are therefore presumably not responsible for any subcellular localization, which would instead rely on a signal sequence. We will better clarify this point in the main text.
Supplemental Figure 2
Before adherens junctions even exist dlg-1 go to the membrane - this is really neat!
Thanks Reviewer #2!
Supplemental Figure 3
Technical question: If either 5 or 3 stack images are used, how does this work? Do they have different z-spacings? Or do they do 5-stack images represent a wider Z-space?
This is the sentence under question: “Maximum intensity projections of 5 (1.08 µm) (A) and 3 (0.54 µm) (B) Z-stacks”. The space between each Z-stack image is constant in all our imaging and its value is 270 nm. When we consider 5 planes, the distance from the 1st to the 5th is 4 x 270 nm = 1.08 µm, whereas for 3 planes will be 2 x 270 nm = 0.54 µm.
Supplemental Figure 4
Line #2 retains translation and keeps mRNA localization.
Totally optional, but consider showing both lines in the main figure to illustrate the two possibilities.
Noted.
Materials and methods - how did they created the ATG mutations? Is it an array? - why does one translate, and one doesn't?
We will clarify this point in Materials and methods: “dlg-1 deletion constructs ΔATG (SM2664 and SM2663) and ΔL27-PDZs (SM2641) were generated by overlap extension PCR using pML902 as a template.”.
We will perform a Western blot to clarify Reviewer #2’s last point. Currently we do not know what peptide is translated, but the comparison with our full-length control will probably shed some light on the issue.
Reviewer #3
Major comments
The smFISH results are striking and implications exciting. The conclusions made from the smFISH results reported in all Figures will be strengthened considerably by quantifying the mRNA localized to the defined specific subcellular regions. At the very least, localization to the cytoplasm versus the plasma membrane should be determined as performed in Figure 2B, but quantifying finer localization will enhance the conclusions made about regional localization (e.g. CeAJ versus plasma membrane mRNA localization in Figure 5). Inclusion of a non-localizing control in Figures 1-4 will enable statistical comparisons between mRNA localizing and non-localizing groups.
We will add more quantitation, statistics, and negative controls.
The script used for smFISH quantitation should be included in the methods or published in an accessible forum (Github, etc). Criteria for mRNA "dot" calling should be defined in the methods. All raw smFISH counts should also be reported.
We will add the full description of the script in Materials and methods, and we will provide the raw data in an additional supplementary table.
Figure 2: What is the localizing ratio of a non-localizing control mRNA (e.g. jac-1)? Including an unlocalized control with quantitation would strengthen the localization arguments presented.
Yes, we will add quantitation for an unlocalized mRNA.
Figure 5: Quantifying colocalization of mRNA and protein (+/- AJM-1) will strengthen the arguments made about mRNA/protein localization.
Yes, we will quantify Fig. S5 to have a full picture of the cells (the images in Fig. 5 represent only a portion of the cell).
Discussion of the CeAJ mRNA localization mechanism is warranted. Do the authors speculate that the newly translated protein drives localization during translation, similar in concept to SRP-mediated localization to the ER, or ribosome association is a trigger to permit a secondary factor to drive mRNA localization, or another model?
Unfortunately, this is hard to say at the moment as we do not have any data regarding where translation actually occurs. We will add a conjecture to the Discussion.
Minor comments
Please complete the following sentence: "We identified transcripts enriched at the CeAJ in a stage- and cell type-specific."
Corrected.
It would be helpful to provide reference(s) for the protein localization summary in Table 1.
Added.
Figure 2B: Did dlg-1 and ajm-1 localize at similar ratios? Appropriate statistics comparing the different ratios may be informative.
We will modify the graph (following Reviewer #2’s suggestion) and add the requested details.
Figure 2: In the paragraph that begins, "Morphogenesis of the digestive track," the text should refer to Figure 2C? If not, the text requires further clarification.
Corrected.
Figure 2: Reporting the smFISH localizing ratios of 8E and 16E will be informative.
We will add the information.
Please include citations when summarizing the nonsense-mediated decay NMD mechanism and AJM-1 identifying the CeAJ.
Added.
The sentence, "Embryos from our second __Δ__ATG transgenic line displayed a little GFP protein and some dlg-1::gfp mRNA," should refer to Figure S4.
Added.
An immunoblot of this reporter versus wild type may be informative regarding the approximate position of putative alternative start codon.
We will perform a Western blot to verify the size of the protein product produced.
Figure 5: N's and repetitions performed should be included for localization experiments.
Yes, we will add them here and in all the other quantifications we will add to the manuscript.
Please clarify that the "the mechanism of UTR-independent targeting is unknown in any species" refers to dlg-1 mRNA localization.
Added.
"Our findings suggest..." discussion paragraph should reference Figure 6.
Added.
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Referee #3
Evidence, reproducibility and clarity
Subcellular localization of mRNAs plays a critical role in gene regulation and ultimately cellular function. While mRNA untranslated regions often serve as key regulatory codes for expression, mRNA translation can also have a significant effect, a notable example being secretory peptides delivering translating transcripts to the endoplasmic reticulum. A complete understanding of the signals that organize mRNAs in the cell remains an open question. Here, Tocchini, et al. use the C. elegans embryo and single molecule FISH (smFISH) to determine the subcellular localization of key mRNAs involved in epithelial morphogenesis. This survey identifies several mRNAs that appear to localize to specific regions of the cell, such as the plasma membrane or apical junction, and in a developmental stage-specific manner. Dissection of the mRNA of dlg-1/discs large, an apical junction component, provides evidence that mRNA localization requires active translation, but surprisingly the untranslated regions are dispensable. Further mRNA truncation mapping supports the model that the N-terminal coding region helps target mRNAs to the apical junctions, but the C-terminal coding regions are sufficient to localize dlg-1 mRNA to the plasma membrane. The manuscript describes a two-step model for dlg-1 localization and recruitment to the apical junction that depends on translation.
MAJOR:
- The smFISH results are striking and implications exciting. The conclusions made from the smFISH results reported in all Figures will be strengthened considerably by quantifying the mRNA localized to the defined specific subcellular regions. At the very least, localization to the cytoplasm versus the plasma membrane should be determined as performed in Figure 2B, but quantifying finer localization will enhance the conclusions made about regional localization (e.g. CeAJ versus plasma membrane mRNA localization in Figure 5). Inclusion of a non-localizing control in Figures 1-4 will enable statistical comparisons between mRNA localizing and non-localizing groups.
- The script used for smFISH quantitation should be included in the methods or published in an accessible forum (Github, etc). Criteria for mRNA "dot" calling should be defined in the methods. All raw smFISH counts should also be reported.
- Figure 2: What is the localizing ratio of a non-localizing control mRNA (e.g. jac-1)? Including an unlocalized control with quantitation would strengthen the localization arguments presented.
- Figure 5: Quantifying colocalization of mRNA and protein (+/- AFM-1) will strengthen the arguments made about mRNA/protein localization.
- Discussion of the CeAJ mRNA localization mechanism is warranted. Do the authors speculate that the newly translated protein drives localization during translation, similar in concept to SRP-mediated localization to the ER, or ribosome association is a trigger to permit a secondary factor to drive mRNA localization, or another model?
MINOR:
- Please complete the following sentence: "We identified transcripts enriched at the CeAJ in a stage- and cell type-specific."
- It would be helpful to provide reference(s) for the protein localization summary in Table 1.
- Figure 2B: Did dlg-1 and ajm-1 localize at similar ratios? Appropriate statistics comparing the different ratios may be informative.
- Figure 2: In the paragraph that begins, "Morphogenesis of the digestive track," the text should refer to Figure 2C? If not, the text requires further clarification.
- Figure 2: Reporting the smFISH localizing ratios of 8E and 16E will be informative.
- Please include citations when summarizing the nonsense-mediated decay NMD mechanism and AJM-1 identifying the CeAJ.
- The sentence, "Embryos from our second ΔATG transgenic line displayed a little GFP protein and some dlg-1::gfp mRNA," should refer to Figure S4. An immunoblot of this reporter versus wild type may be informative regarding the approximate position of putative alternative start codon.
- Figure 5: N's and repetitions performed should be included for localization experiments.
- Please clarify that the "the mechanism of UTR-independent targeting is unknown in any species" refers to dlg-1 mRNA localization.
- "Our findings suggest..." discussion paragraph should reference Figure 6.
Significance
This well-written, well-cited manuscript describes the striking subcellular localization pattern of a critical, conserved gene involved in both animal development and human disease. The observation that the start codon, and thus translation, is necessary for transcript localization is a complete surprise, and opens exciting doors to investigate how translation leads to mRNA organization and its connection to tissue development. As such, this manuscript will be of broad interest to RNA, cell and developmental biologists, particularly those who investigate post-transcriptional gene regulation and protein complex assembly. However, while the images are indeed supportive of the manuscript's claims, the conclusions will be markedly strengthened by quantifying the subcellular localization of mRNAs in the smFISH experiments, paired with negative controls (e.g. non-localizing, cytoplasmic mRNA). Addition of more quantitative smFISH analyses will enhance the experimental reproducibility, rigor, and statistical significance. The text, figures, and methods should also be revised to include more details about the smFISH analyses, in particular the inclusion of n's, descriptions of how spots were identified, descriptions of scripts used, and the raw mRNA counts. Regardless, the reporter genes tested were well conceived and dlg-1 shows promise to be a fantastic model to further investigate the mechanisms underlying translation-dependent mRNA localization.
My expertise covers post-transcriptional gene regulation, the C. elegans model organism, and fluorescent imaging with smFISH.
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Referee #2
Evidence, reproducibility and clarity
Summary:
Tocchini et al. screened apical junction and cell membrane proteins for mRNA localization. They identified multiple proteins that are translated from localized mRNAs. Of these, dlg-1 (Discs large) mRNA localizes to cell cortices of dorsal epithelial cells, endoderm cells, and epidermal (seam) cells and is dependent on active translation for transport. The manuscript dissects the contributions of different DLG-1 protein domains to mRNA localization.
A major strength of the paper is the way it assesses translational-dependence in a transcript-specific way without perturbing translation globally. The authors cleverly combine mutations in ATG start sites with a knock down of the non-sense mediated decay pathway. This allows Tocchini et al to examine whether dlg-1 mRNA depends on active translation for localization, which it does. The authors observe an interesting finding, that the domains required for protein localization can be separated from those required for mRNA localization. Namely, mRNA localization (but not protein localization) requires C-terminal domains of the protein.
My major points of concern focus on the presentation and interpretation of Figure 5. In this figure, the blocking approach used seems confounding, the observations described by the authors are not visible, the quantification is confusing, and the interpretations seem like an over-reach. The
Major comments:
• Figure 2 requires a negative (or uniformly distributed) mRNA control for comparison. Figure 2C should be quantified. The plot quality should be improved, and appropriate statistical tests should be employed to strengthen the claimed findings.
• Most claims of perinuclear mRNA localization are difficult to see and not well supported visually or statistically. The usage of DAPI markers, membrane markers, 3D rendering, or a quantified metric would bolster this claim. Also, sax-7 is claimed to be perinuclear and elsewhere claimed to be uniform then used as a uniform control. Please explain or resolve these discrepancies more clearly.
• The major concern about the paper is the data display and interpretation of Figure 5C. I'm not comfortable with the approach the authors took of blurring out the nucleus. A more faithful practice would be to use an automated mask over DAPI staining or to quantify the entirety of the cell. If the entirety of the cell were quantified, one could still focus analysis on specific regions of relevance. The interpretations distinguishing membrane versus cytoplasmic localization (or mislocalization) are hard to differentiate in these images especially since they are lacking a membrane marker. The ability to make these distinctions forms the basis of Tocchini et al's two pathways of dlg-1 mRNA localization. These interpretations also heavily rely on how the image was processed through the different Z-stacks, and it's not clear to me how that was done. For example, the diffusion of mRNA in figure 5F and 5I are indistinguishable to my eye but are claimed to be different.
• To my eye, it seems that Figure 5 could be more faithfully interpreted to state that DGL-1 protein localization depends on the L27-SH3 domains. The Huk/Guk domains are dispensable for DLG-1 protein localization; however, through other studies, we know they are important for viability. In contrast, dlg-1 mRNA localization requires all domains of the protein (L27-Guk). It is exceptionally interesting to find a mutant condition in which the mRNA and protein localizations are uncoupled. It would be very interesting to explore in the discussion or by other means what the purpose of localized translation may be. Because, in this instance, proper mRNA localization and protein function are closely associated, it may suggest that DLG-1 needs to be translated locally to function properly.
• The manuscript requires an improve materials & methods description of the quantification procedures and statistics employed.
Minor & Major comments together:
Text
• Summary statement: Is "adherent junction" supposed to be "adherens junction?"
• Abstract: Sentence 1, I think they should add a caveat word to this sentence. Something like "...phenomenon that can facilitate sub-cellular protein targeting." In most instances this isn't very well characterized or known.
• In the first paragraph, it might be good to mention that Moor et al also showed that mRNA localize to different regions to alter their level of translation (to concentrate them in high ribosome dense regions of the cell).
• There are some new studies of translation-dependent mRNA localization - that might be good to highlight - Li et al., Cell Reports (PMID: 33951426) 2021; Sepulveda et al., 2018 (PCM), Hirashima et al., 2018; Safieddine, et al 2021. Also, Hughes and Simmonds, 2019 reviews membrane associated mRNA localization in Drosophila. And a new review by Das et al (Nat Rev MCB) 2021 is also nice.
• Parker et al. did not show that the 3'UTR was dispensable for mRNA localization. They showed the 3'UTR was sufficient for mRNA localization.
• In the second paragraph, the sentence about bean stages is missing one closing parenthesis.
• Last paragraph: FISH is fluorescence, not fluorescent.
• Both "subcellular" and "sub-cellular" are used. Minor comments - Figures
• Figure 1
o Figure 1A is confusing. It's not totally clear what the rectangles and circles signify. There are many acronyms within the figure. Which of the cell types depicted in the figure are shown here? For example, for the dorsal cells, which is the apical v. basal side? o Some of the colors are difficult to distinguish, particularly when printed out or for red/green colorblind readers. Is erm-1 meant to be a cytoskeletal associated or a basolateral polarity factor? o The nomenclature for dlg-1 is inconsistent within "C". o Please specify what the "cr" is in "cr.dlg-1:-gfp" in the legend.
• Figure 2
o Can Figure 2C be quantified in a similar manner to 2A/2B? o 2B - please jitter the dots to better visualize them when they land on top of one another o Please include a negative control example, a transcript that is not peripherally localized for comparison. o There is no place in the text of the document where Fig 2C is referenced o I can't see any discernable ajm-1 localization in Fig 2A. o I can't see any dlg-1 pharangeal localization in Fig2C. o More details on how the quantification was performed would be welcome. Particularly, in 2B, what is the distance from the membrane in which transcripts were called as membrane-associated? What statistics were used to test differences between groups?
• Figure 3
o Totally optional but might be nice: can you make a better attempt to approximate the scale of the cartoon depiction? o The GFP as an asterisk illustration may be confusing for some readers. Could you add another rectangular box to depict the gfp coding sequence? o This microscopy is beautiful! o Were introns removed? Is the endogenous copy still present? o The wording in the legend "CRISPR or transgenic" may be confusing as Cas9 genome editing is still a form of transgenesis. o The authors state that the 5'-3'UTR construct produces perinuclear dlg-1 transcripts but in the absence of DAPI imaging, it's not clear that this is the case. o Which probeset was used? The gfp probe? o Here, sax-7 is used as a uniform control, but sax-7 is claimed in Fig S1B-D as being perinuclear. This is a bit confusing.
• Figure 4
o Excellent results! Really nice! o Fig 4A. The GFP depicted as a circle is strange. o Fig 4A. Can you include the gene/protein name for easy skimming? o Fig 4B. the color here is too faint and it is unclear what is being depicted. Overall, this part of the figure could be improved. o Were the introns removed?
• Figure 5
o Fig 5A. can you add the gene/protein name o Fig 5B. Can you you make the example apicobasal (non-apical) mRNA more distinctive? If it had its own peak in the lower trace, the reader would more clearly understand that this mRNA will be excluded from apical measurements whereas it will be included in apicobasal measurements. o D' - I' The grey font is too light. o D' - I' The inconsistent y-axis scaling makes it difficult to compare across these samples. Can you set them to the same maximum number? o D' - I' The x-axis labels are formatted incorrectly o The practice of masking out the nucleus appears to remove potentially important mRNAs that are not nuclear localized. This could really impact the findings and interpretation. Instead, consider an automated DAPI mask. o I can't see what the authors are calling membrane diffuse versus cytoplasmic. This is making it hard for me to see their "two step" pathway to localization. o "F" looks the same as "I" to me, but the authors claim they represent different patterns and use these differences as the basis for their claim that X. o Can more details of the quantification be included? How were Z-sections selected, chosen for inclusion? Which Z-sections and how many were selected? o Also, why do these measurements focus on what I think are the seam cells when Lockwood et al., 2008 show the entire epithelium that is much easier to see? o Please name these constructs to correlate the text more explicitly to the figures. o How many embryos were analyzed for each trace? How many embryos showed consistent patterns? o Why were these cells used for study here? Lockwood et al., 2008 use a larger field of epithelial cells for visualization.
• Figure 6
o There are major discrepancies between what this figure is depicting graphically and what is described in the text. Again, I'm not comfortable making the "two step" claims this figure purports given the data shared in Figure 5.
Minor comments - Tables & Supplemental Figures
Table 1
• I think this table could be improved to more clearly illustrate which mRNAs were tested and what their mRNA localization patterns were (for example, gene name identifiers included, etc). Could the information that is depicted by gray shading instead be added as its own column? For example, have a column for "Observed mRNA localization"
• Can you add distinct column names for the two columns that are labeled as "protein localization - group"
• Can you also add which of these components are part of ASI v. ASII (as described in the introduction? Supplemental Figure 1
• It is hard to see that some of these spots are perinuclear. More information (membrane marker, 3D rendering, improved metrics) is required to support this claim.
• What do these images look like over the entire embryo, not just in the zoomed in section?
• sax-7 localization in S4 looks similar but a different localization claim is made.
Supplemental Figure 2
• Before adherens junctions even exist dlg-1 go to the membrane - this is really neat! Supplemental Figure 3
• Technical question: If either 5 or 3 stack images are used, how does this work? Do they have different z-spacings? Or do they do 5-stack images represent a wider Z-space?
Supplemental Figure 4
• Line #2 retains translation and keeps mRNA localization.
• Totally optional, but consider showing both lines in the main figure to illustrate the two possibilities.
• Materials and methods - how did they created the ATG mutations? Is it an array? - why does one translate, and one doesn't?
Significance
The authors discover that dlg-1, ajm-1, and hmr-1 mRNAs (among others) are locally translated, and this represents an important conceptual advance in the field as these are well studied proteins and important markers. This is the first study to illustrate translation-dependent mRNA localization in C. elegans, to my knowledge. The mechanisms transporting these mRNAs and their associated translational complexes to the membrane may represent a new pathway of mRNA transport and is therefore significant. The authors identify domains within DLG-1 responsible which is a nice advance. If they are unable to order the events of association as they claim in Figure 5 (and that I dispute), this doesn't detract from the impact of the paper.
Other high-profile studies have recently been published that echo how mRNA localization to membranes can be observed for transcripts that encode membrane-associated proteins (Choaib et al., Dev Cell, 2020; Li et al., Cell Reports, 2021 (PMID: 33951426); and Reviewed in Hughes & Simmonds, Front Gen, 2019). These recent findings underscore the impact of Tocchini et al.'s paper. Similar studies have identified mRNAs localizing through translation dependent mechanisms to a variety of different regions of the cell (Sepulveda et al., eLife, 2018; Hirashima et al., Sci Reports, 2018; Safieddine, et al., Nat Comm, 2021; and reviewed in Ryder et al., JCB 2020). Given the timely nature of these findings and the recent interest in these concepts, a broad readership of readers should be interested in this paper.
My field of expertise is in mRNA localization imaging and quantification. I feel sufficiently qualified to evaluate the manuscript on all its merits.
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Referee #1
Evidence, reproducibility and clarity
Summary:
In the current study Tocchini et al analyze mRNA localization during development of Caenorhabditis elegans embryonic epithelia. Using smFISH-based method they have identified mRNAs associated with the cell membrane or cortex, and with apical junctions. They showed that most of mRNAs involved in AS-II cell adhesion system localize to the membrane. To examine how epithelial morphogenesis affects mRNA localization, authors studied two transcripts encoding DLG-1 and AJM-1 that form a complex. Data showed that studied mRNAs enrichment at the CeAJ varies at distinct stages and cell types of embryogenesis. Then the study was focused on one of the identified transcripts - dlg-1/discs large. Using transgenic lines authors demonstrated that dlg-1 localization to the CeAJ is UTRs-independent, but requires active translation. Moreover, authors mapped protein domains involved in that process.
Major comments:
Fig. 1: Main and supplementary figures present smFISH signals for eight localized mRNAs, while in the results section authors describe that they analyzed twenty-five transcripts. Authors should explain the choice of transcripts presented in the paper. Moreover, smFISH signal of different localized mRNAs in epidermal cells was visualized at different stages (bean, comma or late comma), and authors did not comment what was the reason of such conditions. This may make transcripts localization results difficult to interpret, as further analysis showed that mRNA localization varied in a stage-specific manner. Did author used smFISH probes designed against endogenous mRNAs for all tested transcripts? Marking dlg-1 mRNA as dlg-1-gfp suggests that smFISH probe was specific for gfp transcript. Is it true? If yes, authors should compare localization of wild-type endogenous dlg-1 mRNA with that of the transcript encoding a fusion protein, to confirm that fusion does not affect mRNA localization.
Fig. 2B: Authors conclude that at later stages of pharyngeal morphogenesis mRNA enrichment at the CeAJ decreased gradually in comparison to comma stage. Data do not show statistically significant decrease in ratio of localized mRNAs - for dlg-1: bean: 0.39{plus minus}0.09, comma: 0.29{plus minus}0.08, 1.5-fold: 0.30{plus minus}0.09; for ajm-1: bean: 0.36{plus minus}0.08, comma: 0.30{plus minus}0.05, 1.5-fold: 0.28{plus minus}0.09.
Fig. 4: What was the difference between the first and the second ΔATG transgenic line? Authors should analyze the size of the truncated DLG-1 protein that is expressed from the second ΔATG transgenic line that localizes to CeAJ. Knowing alternative ATGs and protein size may suggest domain composition of the truncated protein. This will allow to confront truncated protein localization with the results from Fig. 5. Moreover, to prove that the localization of dlg-1 mRNA at the CeAJ is translation-dependent, additional experiment should be performed where transcripts localization will be analyzed in embryos treated with translation inhibitors such as cycloheximide (translation elongation inhibitor) and puromycin (that induces premature termination).
Minor comments:
In the introduction section authors should emphasize the main goal and scientific significance of the paper. Fig 1A: It's hard to distinguish different colors on the schematics. Schematics presents intermediate filaments that are not included in the Table 1.
Fig. 1C: dlg-1 transcript is marked as dlg-1-gfp on the left panel and dlg-1 on the right panel.
Fig. 2B: Axis labels and titles are not visible, larger font size should be used.
Fig. 5C: Enlarge the font size.
Fig. S2: Embryonic stages should be marked on the figure for easier interpretation.
Significance
This study provides a few contributions into understanding mRNA localization in Caenorhabditis elegans during embryo development. Firstly, it identifies adhesion system II mRNAs associated with epithelial cells. Secondly, it demonstrates a case study of translation-dependent dlg-1/DLG-1 mRNA localization mechanism that does not involve zip codes. Finally, it provides a model showing the roles of different DLG-1 domains in dlg-1 localization. The results are compelling and experiments are well presented, although in my opinion authors should provide a stronger evidence to support the idea that active translation is essential for dlg-1 localization.
Overall, I believe the work will have a wide appeal covering areas such as mRNA localization, developmental biology and embryogenesis.
My field of expertise is in the RNA-protein interactions and mRNA turnover using biochemical methods as well as in vivo studies in C. elegans and mammalian cell lines. I do not have an expertise in smFISH-based methods.
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Reply to the reviewers
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Reply to the Reviewers
We thank the Referees for their evaluation and their useful comments.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
The MS from Bonaventure and colleagues used a CRISPR to identify novel IFN-induced antiviral effectors targeting HIV-1. One hit, the DEAD Box helicase DDX42, while not itself part of the IFN response, exerts a substantial inhibitory effect on HIV-1 replication when over expressed, and gives a several fold boost to viral replication when knocked down in cells. The effect of DDX42 KO or O/E is manifest at reverse transcription and PLA analysis suggests and interaction with incoming virions. Moreover, DDX42 appears to exert an inhibitory effect generally against retroviruses and retroelements, with evidence that it associates with viral/transposon RNA. The authors further show that DDX42 has antiviral against a range (but not all) RNA viruses, with very striking phenotypes seen especially with Zika, CHIKV and SARS CoV2, with DDX42 associating with dsRNA in infected cells. These data suggest DDX42 is a constitutively expressed a broad-spectrum inhibitor of a range of mammalian RNA viruses. The manuscript is very well written, the data is of good quality and clearly DDX42 is having a general effect on viral replication. The results are novel, important and potentially of wide interest. Where the MS is somewhat lacking is understanding whether DDX42 has direct antiviral activity or is globally affecting cellular RNA metabolism. Some important areas for the authors to consider are:
DDX42 has a potential role in splicing and/or RNA metabolism so I think it would be important to see whether there is any clear global change in gene expression in knockout or knockdown cells cells vs control that might be suggestive of a generalized effect.
Responses
We thank the reviewer for this important question. Indeed, DDX42 didn’t impact the replication of 2 negative strand RNA viruses and this suggested that DDX42 didn’t have a global impact on the target cells, but we could not formally exclude a generalized effect. Therefore, we have performed RNA-seq analysis in order to evaluate the impact of DDX42 depletion (using 3 different siRNAs targeting DDX42 in comparison to a CTRL siRNA in U87-MG cells, and 2 different siRNA in comparison to a CTRL siRNA in A549-ACE2 cells, in samples obtained in 3 independent silencing experiments). The RNA-seq data (See Supplemental File 1 and Figure S5) showed that only 63 genes are commonly differentially expressed by the 3 siRNAs targeting DDX42 in U87-MG cells and only 23 of these genes were also found differentially expressed in A549-ACE2 cells depleted for DDX42. Importantly, the identity of these genes could not explain the observed antiviral phenotypes. These data are in favor of the absence of generalized effect on the target cells, which could have explained the antiviral phenotypes of the sensitive viruses.
• The HIV experiments in primary cells are only one round at present. Does the DDX42 knockdown enhance viral replication in multiround? Does it lead to more viral PAMPs for PRRs to induce IFN?
Responses
We agree with the reviewer that it would have been very informative to measure the impact of DDX42 knockdown in multiround infections in primary T cells. However, we tried several times to do this experiment (with primary T cells from several donors) and we were not successful: indeed, DDX42 KO appeared to slow down cell division, which could be taken into account for a short, one-cycle experiment (i.e. 24 h) 3 days post-Cas9/sgRNA electroporation by adjusting the number of cells at the time of infection. However, DDX42 KO appeared quite toxic in longer experiments, with cells stopping to grow.
The question regarding the generation of more viral PAMPs for PRRs to induce IFN is also very interesting. We know from published work (including ours) that primary T cells don’t normally produce IFN following HIV-1 infection (see for instance Bauby and Ward et al, mBio 2021). However, one can indeed hypothesize that as more viral DNAs are produced in the absence of DDX42, perhaps the primary T cells could detect them and produce IFN. To address this question in primary T cells, we would have needed to be able to perform multiround infections, which was not possible, as mentioned above. Moreover, we could not test this hypothesis in the cell lines that we used, such as U87-MG/CD4/CXCR4 cells, as they are unable to produce IFN following HIV-1 infection.
More could be made mechanistically of the lack of sensitivity of Flu and VSV to DDX42. In particular showing whether or not DDX42 interacts with the RNA of the insensitive virus, or whether DDX42/virus or dsRNA interactions by PLA occur with Flu would highlight the relevance of these observations to the antiviral mechanism.
Responses
This is an excellent remark. We have now performed RNA immunoprecipitation experiments using 2 viruses targeted by DDX42 (CHIKV and SARS-CoV-2) and 1 virus that is insensitive to DDX42 (IAV) (See New Figure 4J-L): whereas CHIKV and SARS-CoV-2 RNAs could be specifically pulled-down with DDX42 immunoprecipitation, this was not the case for IAV RNA. This strongly argues for a direct mechanism of action of DDX42 helicase on viral RNAs.
Reviewer #1 (Significance (Required)):
__ The role of helicases in host defence are of wide interest and importance. This has the potential to be a very important study that deserves a wide audience. However in my opinion it needs some further mechanistic insight along the lines I have suggested.
Responses
As mentioned above, we have now added important data: First, DDX42 is able to interact with RNAs from targeted viruses (and not from an insensitive virus); Second, we have checked that DDX42 didn’t have a substantial impact on the cell transcriptome. Taken together, these data are clearly in favour of a direct mode of action of DDX42.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
In this brief report, the authors use a CRISPR screening approach to identify cellular proteins that limit HIV infection. The screen itself is elegantly designed and most of the top hits are components of the interferon signaling pathway that would be expected to emerge from such a screen, thus providing confidence in the results. The authors followed up on DDX42 as a new hit identified in their screen and confirmed that targeting DDX42 with distinct guide RNAs resulted in increased HIV infection in at least 3 cell lines. Conversely, DDX42 overexpression inhibited infection. They also confirmed a role for DDX42 in inhibiting HIV infection in primary macrophages and CD4 T cells using siRNA and CRISPR KO strategies, respectively. They also demonstrate that DDX42 inhibits several other divergent lentiviruses as well as Chikungunya virus and SARS-CoV-2, but not influenza virus. These data convincingly show that DDX42 plays a role in inhibiting many lentivirus and positive sense RNA virus infections. Using PCR assays for reverse transcription products they conclude that DDX42 inhibits an early process in the HIV life cycle occurring after virus entry, though the statistical significance of these differences is not clear. They further use proximity ligation assays to suggest that DDX42 is in proximity to HIV-1 and SARS-CoV-2 replication complexes. Mechanistically, these data are largely unsatisfying as they do not provide specific insight into how DDX42 so broadly inhibits virus replication. Overall, the manuscript presents a significant advance, it also has some weaknesses as listed below.
Statistical analysis is not included in any of the figures.
Response
Statistical analyses have now been included.
Many of the figure legends do not state how many independent biological replicates the figures are based on.
Response
The number of biological replicates for each panel is stated at the very end of each figure legend.
Detailed mechanistic understanding of DDX42 effects on virus replication is not provided by the manuscript.
Response
As mentioned in response to Reviewer 1, we have now added data showing that DDX42 could interact with RNAs from targeted viruses but not from an insensitive virus, arguing for a direct antiviral mode of action of this Dead-Box helicase.
Reviewer #2 (Significance (Required)):
DDX42 is a new antiviral protein identified and confirmed in this manuscript. It was also identified as one of many hits in a genome wide CRISPR screen for cellular proteins that regulate SARS-CoV-2 infections, but was not followed up. Thus, the identification and confirmation of DDX42 antiviral activity is highly significant for both the HIV and SARS-CoV-2 fields. This high significance may compensate to some extent for the lack of mechanistic insight contained in this initial report.
**Referees Cross-commenting**
I find the comments of the other reviewers to be fair and reasonable, and I concur that the work is overall important and novel. It seems that reviewers generally agreed that some additional mechanistic insights would be desirable for publication in a high impact journal. Reviewer 1 makes some good suggestions in this regard. As for mouse experiments, I would reserve these for a follow up manuscript.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
__In this manuscript, Bonaventure et al report the results of a screen to identify cellular inhibitors of HIV-1 infection in IF treated cells. They identify DDX42 as such a factor though, unexpectedly, DDX42 did not turn out to be an ISG. Strikingly, DDX42 turns out to inhibit a wide range of retroviruses as well as retrotransposons and + sense, but not - sense, RNA viruses among which SARS-CoV2 turns out to be especially sensitive to DDX42, with siRNAs specific for SARS-CoV2 DDX42 increasing viral RNA expression by a startling 3 orders of magnitude, compared to only an 2-5 fold positive effect with HIV-1.
Response
We agree with the reviewer that DDX42’s impact on HIV-1 may appear as somewhat modest, however, it is highly reproducible across cell lines and primary cells and, more importantly, it is observed upon depletion of the endogenous protein (either by KO or silencing) in target cells that are highly permissive to viral replication, such as activated primary CD4+ T cells. We therefore believe that these findings, combined with the findings that other positive-strand RNA viruses are targeted, are of high interest.
Reviewer #3 (Significance (Required)):
__I found this paper generally convincing and technically sound though the emphasis was odd and clearly driven more by the history of how this work was done than by the actual results obtained. Specifically, the emphasis is on HIV-1 yet the most interesting data are the dramatic effects seen with Chikungunya and SARS2. If I was writing this paper, I would delete figure 4 and focus this paper entirely on retroviruses and retrotransposons. In that form, I think it would be competitive at PLoS Pathogens or perhaps EMBO Journal. The RNA virus work shown in figure 4 could then be figure 1 of a new, high impact, paper looking at the mechanism of action of DDX42 as an inhibitor of + sense, but not - sense, viral gene expression. Though Wei et al do mention DDX42 in their SARS-CoV2 screening paper this is certainly not a major theme of that paper so I don't think that would be a problem.
Responses
We thank the reviewer for this comment. We had hesitated to present the manuscript as suggested by the reviewer (i.e. focusing only on HIV-1, retroviruses and retroelements) and prepare a second manuscript with the remaining data. We’ve finally decided against it, as we believe that showing a broad antiviral effect of DDX42 on +strand RNA viruses increases the impact of our findings.
On another note, a conditional DDX42 KO mouse has been generated by the Wellcome trust Sanger institute and it would greatly improve this manuscript if they could show an in vivo a result similar to figure 3F using MLV.
Responses
We thank the reviewer for this information. We completely agree that in vivo work would be a massive plus and we will be planning to explore this in the future, but not at this stage as it would require specific funding and resources.
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Referee #3
Evidence, reproducibility and clarity
In this manuscript, Bonaventure et al report the results of a screen to identify cellular inhibitors of HIV-1 infection in IF treated cells. They identify DDX42 as such a factor though, unexpectedly, DDX42 did not turn out to be an ISG. Strikingly, DDX42 turns out to inhibit a wide range of retroviruses as well as retrotransposons and + sense, but not - sense, RNA viruses among which SARS-CoV2 turns out to be especially sensitive to DDX42, with siRNAs specific for SARS-CoV2 increasing viral RNA expression by a startling 3 orders of magnitude, compared to only an 2-5 fold positive effect with HIV-1.
Significance
I found this paper generally convincing and technically sound though the emphasis was odd and clearly driven more by the history of how this work was done than by the actual results obtained. Specifically, the emphasis is on HIV-1 yet the most interesting data are the dramatic effects seen with Chikungunya and SARS2. If I was writing this paper, I would delete figure 4 and focus this paper entirely on retroviruses and retrotransposons. In that form, I think it would be competitive at PLoS Pathogens or perhaps EMBO Journal. The RNA virus work shown in figure 4 could then be figure 1 of a new, high impact, paper looking at the mechanism of action of DDX42 as an inhibitor of + sense, but not - sense, viral gene expression. Though Wei et al do mention DDX42 in their SARS-CoV2 screening paper this is certainly not a major theme of that paper so I don't think that would be a problem. On another note, a conditional DDX42 KO mouse has been generated by the Wellcome trust Sanger institute and it would greatly improve this manuscript if they could show an in vivo a result similar to figure 3F using MLV.
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Referee #2
Evidence, reproducibility and clarity
In this brief report, the authors use a CRISPR screening approach to identify cellular proteins that limit HIV infection. The screen itself is elegantly designed and most of the top hits are components of the interferon signaling pathway that would be expected to emerge from such a screen, thus providing confidence in the results. The authors followed up on DDX42 as a new hit identified in their screen and confirmed that targeting DDX42 with distinct guide RNAs resulted in increased HIV infection in at least 3 cell lines. Conversely, DDX42 overexpression inhibited infection. They also confirmed a role for DDX42 in inhibiting HIV infection in primary macrophages and CD4 T cells using siRNA and CRISPR KO strategies, respectively. They also demonstrate that DDX42 inhibits several other divergent lentiviruses as well as Chikungunya virus and SARS-CoV-2, but not influenza virus. These data convincingly show that DDX42 plays a role in inhibiting many lentivirus and positive sense RNA virus infections. Using PCR assays for reverse transcription products they conclude that DDX42 inhibits an early process in the HIV life cycle occurring after virus entry, though the statistical significance of these differences is not clear. They further use proximity ligation assays to suggest that DDX42 is in proximity to HIV-1 and SARS-CoV-2 replication complexes. Mechanistically, these data are largely unsatisfying as they do not provide specific insight into how DDX42 so broadly inhibits virus replication. Overall, the manuscript presents a significant advance, it also has some weaknesses as listed below.
- Statistical analysis is not included in any of the figures.
- Many of the figure legends do not state how many independent biological replicates the figures are based on.
- Detailed mechanistic understanding of DDX42 effects on virus replication is not provided by the manuscript.
Significance
DDX42 is a new antiviral protein identified and confirmed in this manuscript. It was also identified as one of many hits in a genome wide CRISPR screen for cellular proteins that regulate SARS-CoV-2 infections, but was not followed up. Thus, the identification and confirmation of DDX42 antiviral activity is highly significant for both the HIV and SARS-CoV-2 fields. This high significance may compensate to some extent for the lack of mechanistic insight contained in this initial report.
Referees Cross-commenting
I find the comments of the other reviewers to be fair and reasonable, and I concur that the work is overall important and novel. It seems that reviewers generally agreed that some additional mechanistic insights would be desirable for publication in a high impact journal. Reviewer 1 makes some good suggestions in this regard. As for mouse experiments, I would reserve these for a follow up manuscript.
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Referee #1
Evidence, reproducibility and clarity
The MS from Bonaventure and colleagues used a CRISPR to identify novel IFN-induced antiviral effectors targeting HIV-1.
One hit, the DEAD Box helicase DDX42, while not itself part of the IFN response, exerts a substantial inhibitory effect on HIV-1 replication when over expressed, and gives a several fold boost to viral replication when knocked down in cells. The effect of DDX42 KO or O/E is manifest at reverse transcription and PLA analysis suggests and interaction with incoming virions. Moreover, DDX42 appears to exert an inhibitory effect generally against retroviruses and retroelements, with evidence that it associates with viral/transposon RNA. The authors further show that DDX42 has antiviral against a range (but not all) RNA viruses, with very striking phenotypes seen especially with Zika, CHIKV and SARS CoV2, with DDX42 associating with dsRNA in infected cells. These data suggest DDX42 is a constitutively expressed a broad-spectrum inhibitor of a range of mammalian RNA viruses.
The manuscript is very well written, the data is of good quality and clearly DDX42 is having a general effect on viral replication. The results are novel, important and potentially of wide interest. Where the MS is somewhat lacking is understanding whether DDX42 has direct antiviral activity or is globally affecting cellular RNA metabolism. Some important areas for the authors to consider are:
• DDX42 has a potential role in splicing and/or RNA metabolism so I think it would be important to see whether there is any clear global change in gene expression in knockout or knockdown cells cells vs control that might be suggestive of a generalized effect.
• The HIV experiments in primary cells are only one round at present. Does the DDX42 knockdown enhance viral replication in multiround? Does it lead to more viral PAMPs for PRRs to induce IFN?
• More could be made mechanistically of the lack of sensitivity of Flu and VSV to DDX42. In particular showing whether or not DDX42 interacts with the RNA of the insensitive virus, or whether DDX42/virus or dsRNA interactions by PLA occur with Flu would highlight the relevance of these observations to the antiviral mechanism.
Significance
The role of helicases in host defence are of wide interest and importance. This has the potential to be a very important study that deserves a wide audience. However in my opinion it needs some further mechanistic insight along the lines I have suggested.
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Reply to the reviewers
General Statements
We appreciate the thoughtful and constructive comments provided by the reviewers and the opportunity to submit our revision plan for consideration. We have copied the reviewers’ comments below and have detailed our proposed revisions and/or clarifications after each comment (or set of comments). We also provide a partially revised manuscript with editorial changes highlighted in red.
Reviewer 1:
In this work, the authors Titialii-Torres and Morris assess how hyperglycemia affects the development of the neural retina using a genetic and a nutritional approach in the model organism zebrafish. This is important as diabetes can contribute to retinal degeneration in during the progression of diabetic retinopathy which often leads to blindness in adults. The authors examine how different cell types in the neural retina are affected in a genetic hyperglycemic model, the pdx1 mutant embryos, and in a nutritional model, in which hyperglycemia is induced by glucose and dexamethasone exposure. Titialii-Torres and Morris show that in both models, photoreceptor rods and cones, as well as horizontal cells, are reduced in number. Additionally, they report a delay in retinal cell differentiation accompanied by increased ROS production in the hyperglycemic retina. Altered expression of metabolism related genes and effects on visual function were also found in their hyperglycemic models. Overall, the assessment of the different retinal cell types impacted by hyperglycemia and examination of potential molecular mechanisms contributes important and novel data to the field. However, the data as presented falls short in supporting the conclusions of the authors.
**Major comments**
Overall, the conclusions would be more strongly supported by improving the clarity of the images, and by additional analyses.
Figure1:
Referring to figure 1 E' the text states that an arrowhead points to the shorter and thinner outer segment of a rod. In the figure there is an arrow pointing to a cell without a visible outer segment, making it hard to make the same conclusion. Additionally the GFP signal is very weak in D and E in the dorsal retina. Therefore it is not possible to see if there is also a decreased amount of rods in the dorsal retina as claimed. In the text it is mentioned that cones in the ventral region are affected. Is there also a difference in the dorsal region?
Response: In our revised manuscript, we will include higher magnification panels for better visualization of the morphological differences between photoreceptor outer segments; we will also revise the graphs to show separate quantification of photoreceptors in the dorsal vs ventral retina.
Figure 3: Rods and cones might be better displayed in close-ups from sections rather than from projections of the whole eye.
Response: We will make this change
The authors write about a reduction of cones upon glucose treatment. In the graph this is not highlighted as significant.
Response: the change is significant; the graph will be edited to indicate this
Figure 4: as the overall number of cones was already assessed before, focusing on a smaller region might help the reader to see the Zpr3 staining showing that the outer segments of the cones are stunted (as stated in the main text). In the figure panels presented, outer segments cannot be clearly seen.
Response: we agree, and will make this change
Figure 6: scale bar is missing. Please clarify what the red and the green is. Why is there a red signal from Mitosox outside of the embryo (panel C)? The fluorescence of the superoxide probe should be displayed in a more convincing way. For example, in sections to enable assignment of signal to tissues and cells, as shown in Supplemental Figure 5.
Response: for the revised manuscript we will replace this figure with one containing analysis of tissue sections, with appropriate figure annotation and scale bar
Figure 8: Is the coincubation with methylene blue leading to a significant increase in photoreceptors? If yes, this should be indicated in the graph.
Response: for methylene blue treatment alone, the increase was not statistically significant; we have added text in the Results to clarify this. For the revised manuscript, we are also performing additional experiments with a methylene blue + SOD treatment group and with other ROS inhibitors, so this figure will be updated with those data.
Supplemental Figure 2: The authors assert that TUNEL+ cell labeling coincides with Müller glial cells. This would be better supported with a magnified view of the INL, optimally by applying TUNEL staining to hyperglycemic, GFAP:GFP transgenic samples.
Response: we will repeat this experiment using the GFAP:GFP line as suggested
It would be of interest to determine if an incubation with methylene blue also affects photoreceptors in pdx1 mutants. Is it possible to confirm that Methylene blue treatment reduces ROS in the retina ? Can changes in ROS response gene expression be demonstrated by qPCR ? The assumptions about ROS should be either strengthened by additional experiments or less emphasized in the discussion.
Response: for the revised version we will include the ROS inhibitor experiments on pdx1 mutants as suggested, as well as imaging with the Mitosox probe to confirm the efficacy of the ROS inhibitors; we are also testing additional ROS inhibitors as described above.
For completeness, glucose metabolism in the genetic model should be also addressed and compared to the nutritional model.
Response: While we agree that it would be helpful to have these data, it would take a very long time to collect the necessary number of pdx1 mutant individuals needed for this experiment due to the small numbers of homozygous mutants recovered in each clutch. As an alternative approach, for the revised manuscript we will use qRT-PCR to test a subset of the genes on the pdx1 mutants that showed significant changes in the nutritional model.
The authors talk about a "long term" return to normoglycemia and long term effects of hyperglycemia. Analysis at 7 dpf after a 2 day return to normoglycemic conditions can hardly be called long term. To make these statements, an assessment after a longer time period (one week or more if possible?) would be more convincing.
Response: for our revised manuscript, we are adding an additional time point for analysis at one week post hyperglycemia
The claims of 'reactive gliosis' in glucose-treated larvae is overstated. Biologically meaningful differences in cell shape between control and treated samples are not evident from the images (Fig. 5A-F). This should at least be quantitated by shape analysis. The Glucose+Dex samples do not show increased number of Müller glial cells, and glucose treatment alone leads to highly variable glucose levels. This complicates and weakens a correlation with hyperglycemia.
Response: we will add the suggested shape quantification of these images; we are also performing Western blots with an anti-GFAP antibody to further strengthen our conclusions – this is a well-accepted method for demonstrating gliosis.
**Minor comments**
Some figures would benefit if they would follow the sequence of the text. Eg: figure 1 and 3, the text addresses first the rods and then the cones. In several places the panels referred to in the text do not match the figures or figure panels are not mentioned at all. For example: Pg 3 "Quantification revealed a significant decrease in both rod and cone photoreceptors in pdx1 mutants at 5 dpf (Fig. 1C)." - the quantification is in panels C and F. The main text does not mention or explain Figure 2A.
Pg 5 "The results confirmed that rods and cones from hyperglycemic larvae have shorter outer segments compared to wild type larvae at 5 dpf (Fig. 4A-C)." - panel C is a graph of Saccades. Fig. S3 - only panel Y is referred to in the text.
Response: the text has been edited to correct these issues
Supplemental figure 2: the authors claim a significant increase of apoptotic cells in the genetic model. In the corresponding graph significance is not indicated.
Response: the increase in apoptotic cells was significant for the nutritional but not the genetic model; the text has been corrected to reflect this.
Figure 5: scale bars are missing, the figure text and the numbering of the figure do not fit.
The suggested corrections will be made to this figure and the corresponding text
Supplemental figures 4 and 5: The Prox1 staining is hard to see and it is unclear what was counted as cells.
Response: annotations will be added to Sup Figs 4 and 5 to clarify which cells are being quantified
In Supp Fig. 4E the PKC staining looks increased compared to the controls.
Response: the variability in staining intensity is within the normal range of what we have observed across all treatments and genotypes
The graphs could have similar y axes, especially because in Supp Fig. 5 the amount of cells/µm is also different. Why not always use per 50µm? Shouldn't the amount of cells in wild types and untreated embryos be the same per 50µm? Also the labelling of the y axes could be made coherent in the two figures.
Response: The denominator will be standardized for all graphs. The scale of the y-axes varies by cell type because some retinal cell classes are significantly more abundant than others.
Supplemental figure 6: K is not mentioned in the legend.
Response: this has been corrected
2-NDBG treatment is not explained in material and methods
Response: this information has been added to the Methods
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Reviewer #1 (Significance (Required)):
**Significance**
Titialii-Torres et al. characterize the impaired development of neural retinal cells under hyperglycemic conditions in zebrafish larvae and also show evidence of impaired visual function. This work will be of interest for researchers in the field of diabetes, especially those focused on diabetic retinopathy, and for developmental biologists interested in pathologies that impact human development. While the manuscript provides insights into the development of the retina under hyperglycemic conditions, a revision addressing weaknesses of figure presentation and some additional confirmatory experiments would be of great benefit.
Response: we appreciate the reviewer’s assessment that our work will be of interest to various research communities, and agree that the suggested revisions to the figures and confirmatory experiments will greatly strengthen the impact.
Reviewer 2:
**Summary:**
This paper uses immersion of embryonic zebrafish in high glucose solution to model the effects of hyperglycemia on retinal development. The paper finds that high glucose causes a reduction in the number of photoreceptors and horizontal cells, abnormalities in the morphology of photoreceptors and Müller glia, increased retinal cell apoptosis, a change in the timing of neuronal cell birth, and a defect in the optokinetic response. The mechanistic link between high glucose and changes in retinal development is not well described but may involve an increase in reactive oxygen species.
**Major comments:**
- Is the photoreceptor phenotype a degenerative rather a developmental phenotype? In embryos treated with high glucose, photoreceptors in the periphery of the retina near the ciliary margin, which are younger in age, seem to be structurally more normal than those at the center, away from the ciliary margin, which are older in age. Could this reflect the fact that photoreceptor development proceeds normally followed by degenerative changes?
Response: this is certainly a possibility, given the increase in TUNEL positive cells we detected in hyperglycemic retinas. However, we did not detect many apoptotic cells in the ONL at 3 and 4 dpf, suggesting that there is not widespread degeneration among differentiated photoreceptors at that stage. This result, in combination with the altered differentiation timing data shown in Figure 7, is what led us to favor a developmental phenotype. In the revised manuscript, we will add text to the Discussion that more thoroughly explores these alternative interpretations.
- For many or most phenotypes the main examined treatment is glucose + dexamethasone. The authors state this combination achieves more uniform glucose concentrations in the embryos as compared to glucose alone. However, dexamethasone may have effects independently of glucose and the dexamethasone only control is not used in some or most experiments. For example in Fig. 3, could dexamethasone alone causes changes in photoreceptor morphology? In the combo treatment, is it possible that some effects are simply due to a synergism of glucose+dex and not because dex causes a more uniformly high intraembryonic glucose?
Response: we have evaluated photoreceptor number and morphology in the dex alone treatment group and found no significant differences. We will add these results to the main text and the supplemental figures.
- It is interesting that hyperglycemic retinas show more neurons born between 2-5 days post fertilization in the RGC layer than in the outer nuclear layer (Fig 7). One interpretation is delayed birth of RGCs after hyperglycemia as the authors suggest. Another interpretation is that non-RGC cell types are in now in the RGC layer; or that some proliferating progenitors persist at 5dpf. Co-localization of EdU with differentiation markers, and EdU analysis after a short pulse of 2 hours would help to nail down if there is developmental delay or something else going on here.
Response: we appreciate the suggestion, and will perform this experiment for the revision
- Do Müller cells go into cycle after high glucose treatment?
Response: this is a great question – we will do a co-localization experiment and add these results to the revised manuscript.
The increase in ROS in Fig. 6 does not seem very convincing. Is the difference between untreated and glucose or glucose/dex treatments statistically significant? I would avoid making too much of this unless some type of phenotype rescue with N-acetylcysteine or vitamin C, or Trolox, can be shown. Methylene blue is a bit non-specific as an antioxidant.
Response: for methylene blue treatment alone, the increase was not statistically significant; we have added text in the Results to clarify this. For the revised manuscript, we are also performing additional experiments with a methylene blue + SOD treatment group and with other ROS inhibitors, so this figure will be updated with those data
Reviewer #2 (Significance (Required)):
The translational significance of the findings is that they might provide a model to study how embryonic hyperglycemia due to maternal diabetes changes embryonic development. Pitfalls include the fact that its relevance to humans is unclear. Is maternal diabetes known to cause visual abnormalities due to abnormal retinal development in newborns? The basic biology significance may be to provide a model to investigate how glucose metabolism is connected to developmental decisions. However it is unclear whether glucose metabolism within retinal cells mediates the observed effects; and the high glucose used here is likely unphysiological as at these developmental stages zebrafish embryos feed from the yolk sac.
Response: yes, maternal diabetes is associated with retinal abnormalities in humans, although there are not many published studies on this topic. In the Discussion, we talked about how our results align with prior clinical studies which documented reduced inner and outer macular thickness in children of diabetic pregnancies. At the suggestion of Reviewer 3, we have added this information to the Introduction as well to highlight the relevance of our study to humans. With respect to the comment about physiological relevance, we feel that the inclusion of the genetic model, which does not rely on high levels of exogenous glucose and yet exhibits a similar photoreceptor phenotype, speaks to this issue.
Reviewer 3: **Summary:**
The authors use a combination of genetic and pharmacological immersion approaches to investigate the effects of hyperglycemia on development of the retina in zebrafish larvae. They demonstrate a rather mild phenotype (though still convincing) such that photoreceptor maturation is delayed/impaired and the Muller glia are also affected. Visual function is modestly impacted, as measured with an assay that can be influenced by motor as well as sensory defects. The authors conclude that altered timing of the differentiation of retinal cells, together with accumulation of reactive oxygen species (ROS) underly the photoreceptor defects and reduced visual function in the hyperglycemic larvae.
**Major comments**
The retinal phenotype related to hyperglycemia is quite subtle, but sufficiently consistent. This phenotype would be more convincing, and lead to more definitive conclusions, if the authors could include some ultrastructural (TEM) information, or even high-resolution/magnification color images of thinner sections processed using conventional histological methods, such as H&E, or toluidine blue/pyronin B. It is difficult to appreciate the features of the apical projections of the photoreceptors in the fluorescently-labeled images.
Response: we are adding higher magnification images to the photoreceptor figures (also suggested by Reviewer 1) and will incorporate an H&E stain as well.
Comparison of zpr1 labeling with the TaC:eGFP transgenic is unfortunate. Ideally the authors would use the pdx1 mutant on this transgenic background. Alternatively, the authors could perform TaC in situ hybridizations.
Response: we have crossed the pdx1 line onto the TaC:eGFP transgenic background and will have this experiment completed for the revision
The visual function defect is also quite mild. The authors should mention that the OKR assay also relies upon motor function, and so the defect may be related to sensory deficit, motor deficit, or both. Larval ERGs would address this issue.
Response: we will add this alternative explanation for the OKR results to the text.
The "reactive gliosis" phenotype is also mild/subtle, and not entirely convincing. More information should be provided regarding what the authors considered an "abnormal shape" of an MG cell body. Ideally, there is an at least somewhat objective means to score normal vs. abnormal and then quantify.
Response: for the revision, we are adding shape quantification and Western blots (please see our response to the similar comment made by Reviewer 1)
In Figure 6 legend, the authors state that superoxide production is increased, but the graph does not appear convincing in this regard, and no statistical evaluation is provided.
Response: for methylene blue treatment alone, the increase was not statistically significant; we have added text in the Results to clarify this. For the revised manuscript, we are also performing additional experiments with a methylene blue + SOD treatment group and with other ROS inhibitors, so this figure will be updated with those data
The authors do not indicate whether they checked datasets for having a normal distribution prior to the selection of a t-test (or ANOVA) for analysis vs. nonparametric tests.
Response: a more thorough description of our statistical analyses will be added to the methods
The model and accompanying text in the Discussion seem overly wordy and speculative. This discussion also does not acknowledge that the effects upon the retina may be indirect, mediated by other tissues that are impacted by hyperglycemia. For example, ocular vascular defects have been described to result from hyperglycemia, over a similar time frame of analysis, and the effects on the retina may be downstream of these defects.
Response: we will revise the Discussion to remove extraneous information and to incorporate alternative mechanisms that could explain the retinal phenotypes induced by hyperglycemia
**Minor comments:**
Introduction - the statement appearing in the Discussion (offspring of diabetic pregnancies had significantly thinner inner and outer macula as well as lower macular volume [43].) should appear in the Introduction to better capture the interest of the reader.
Response: this change has been made
Page 1. (..in nearly 10% of US pregnancies) - citation needed.
Response: this has been added
Page 2. Pdx1 mutation should be briefly described when first mentioned.
Response: this has been added
Legend for Figure 2 could benefit from a definition of 2-NDBG.
Response: the figure legend has been revised
Figure 2B does not show Whole Body [Glucose] because the heads were removed for histological analysis.
Response: this correction will be made to the figure
It is this reviewer's experience and opinion that zpr-3 labels rods and the RH2 members of the double cones, due to the sequence similarity of RH1 (rhodopsin) and RH2. The cited paper (Yin et al., 2012) hints at this as well, but is slightly unclear due to the terminology used in the paper in describing cone subtypes.
We have edited the Results to clarify that Zpr3 labels the Rh2-expressing member of the double cones
Page 8. The marker used to detect bipolar neurons should be mentioned within the Results section.
Response: this information has been added to the Results
Pages 12-13. The localization of TUNEL+ profiles may be related to microglia extending processes into the ONL, engulfing photoreceptors, and then internally transporting the bits to their cellular "eating stations" within other retinal layers.
Response: we will add text to the Results including this as a possibility. We are also (at the suggestion of Reviewer 1) adding an experiment to determine whether some of the TUNEL+ cells co-localize with Muller glia markers.
Reviewer #3 (Significance (Required)):
**Significance/Comparison to published knowledge:**
The zebrafish model(s) are sufficiently novel, versatile, and interesting to constitute an advance in this field. A literature search by this reviewer revealed that the focus upon retinal cells in hyperglycemic, larval zebrafish appears novel. However, the phenotype is remarkably mild, and there is concern that follow-up studies in pursuit of more mechanistic insights will be challenging to perform by the authors and by others in the field. This paper does lay some key groundwork, but what comes next sounds like a lot of fishing expeditions.
Response: we appreciate the reviewer’s assessment that our work represents a novel advance in this field, and lays “key groundwork” for future studies. Although our nutritional and genetic models do not present with photoreceptor loss so severe that it causes complete blindness at the timepoints we tested, the photoreceptor reductions we observe are consistent, readily scoreable, and are associated with demonstrable defects in visual behavior. Given that we also provide evidence of both altered cell differentiation kinetics and increased oxidative stress in embryonic hyperglycemic retinas, we feel that these are excellent starting places for future work to uncover more mechanistic insights. Finally, our results have implications for human visual system development under hyperglycemic conditions. Timely vision development in infancy is required for attainment of a host of developmental milestones. Even mild delays in this process could have long term consequences for intellectual and social development, and due to the difficulty of measuring visual acuity in infants, subtle but significant impairments may go undetected at this critical stage. Therefore, having a reliable animal model for embryonic hyperglycemia will facilitate efforts to better understand this condition with the goal of developing appropriate intervention and treatment strategies.
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Referee #3
Evidence, reproducibility and clarity
Summary:
The authors use a combination of genetic and pharmacological immersion approaches to investigate the effects of hyperglycemia on development of the retina in zebrafish larvae. They demonstrate a rather mild phenotype (though still convincing) such that photoreceptor maturation is delayed/impaired and the Muller glia are also affected. Visual function is modestly impacted, as measured with an assay that can be influenced by motor as well as sensory defects. The authors conclude that altered timing of the differentiation of retinal cells, together with accumulation of reactive oxygen species (ROS) underly the photoreceptor defects and reduced visual function in the hyperglycemic larvae.
Major comments:
The retinal phenotype related to hyperglycemia is quite subtle, but sufficiently consistent. This phenotype would be more convincing, and lead to more definitive conclusions, if the authors could include some ultrastructural (TEM) information, or even high-resolution/magnification color images of thinner sections processed using conventional histological methods, such as H&E, or toluidine blue/pyronin B. It is difficult to appreciate the features of the apical projections of the photoreceptors in the fluorescently-labeled images.
Comparison of zpr1 labeling with the TaC:eGFP transgenic is unfortunate. Ideally the authors would use the pdx1 mutant on this transgenic background. Alternatively, the authors could perform TaC in situ hybridizations.
The visual function defect is also quite mild. The authors should mention that the OKR assay also relies upon motor function, and so the defect may be related to sensory deficit, motor deficit, or both. Larval ERGs would address this issue.
The "reactive gliosis" phenotype is also mild/subtle, and not entirely convincing. More information should be provided regarding what the authors considered an "abnormal shape" of an MG cell body. Ideally, there is an at least somewhat objective means to score normal vs. abnormal and then quantify.
In Figure 6 legend, the authors state that superoxide production is increased, but the graph does not appear convincing in this regard, and no statistical evaluation is provided.
The authors do not indicate whether they checked datasets for having a normal distribution prior to the selection of a t-test (or ANOVA) for analysis vs. nonparametric tests.
The model and accompanying text in the Discussion seem overly wordy and speculative. This discussion also does not acknowledge that the effects upon the retina may be indirect, mediated by other tissues that are impacted by hyperglycemia. For example, ocular vascular defects have been described to result from hyperglycemia, over a similar time frame of analysis, and the effects on the retina may be downstream of these defects.
Minor comments:
Introduction - the statement appearing in the Discussion (offspring of diabetic pregnancies had significantly thinner inner and outer macula as well as lower macular volume [43].) should appear in the Introduction to better capture the interest of the reader.
Page 1. (..in nearly 10% of US pregnancies) - citation needed.
Page 2. Pdx1 mutation should be briefly described when first mentioned.
Legend for Figure 2 could benefit from a definition of 2-NDBG.
Figure 2B does not show Whole Body [Glucose] because the heads were removed for histological analysis.
It is this reviewer's experience and opinion that zpr-3 labels rods and the RH2 members of the double cones, due to the sequence similarity of RH1 (rhodopsin) and RH2. The cited paper (Yin et al., 2012) hints at this as well, but is slightly unclear due to the terminology used in the paper in describing cone subtypes.
Page 8. The marker used to detect bipolar neurons should be mentioned within the Results section.
Pages 12-13. The localization of TUNEL+ profiles may be related to microglia extending processes into the ONL, engulfing photoreceptors, and then internally transporting the bits to their cellular "eating stations" within other retinal layers.
Significance
Significance/Comparison to published knowledge:
The zebrafish model(s) are sufficiently novel, versatile, and interesting to constitute an advance in this field. A literature search by this reviewer revealed that the focus upon retinal cells in hyperglycemic, larval zebrafish appears novel. However, the phenotype is remarkably mild, and there is concern that follow-up studies in pursuit of more mechanistic insights will be challenging to perform by the authors and by others in the field. This paper does lay some key groundwork, but what comes next sounds like a lot of fishing expeditions.
Interested audiences:
Investigators in vision science/ophthalmology, developmental biology, toxicology/teratology, and diabetes.
Reviewer keywords:
Developmental biology, genetics, retina, zebrafish, photoreceptors.
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Referee #2
Evidence, reproducibility and clarity
Summary:
This paper uses immersion of embryonic zebrafish in high glucose solution to model the effects of hyperglycemia on retinal development. The paper finds that high glucose causes a reduction in the number of photoreceptors and horizontal cells, abnormalities in the morphology of photoreceptors and Müller glia, increased retinal cell apoptosis, a change in the timing of neuronal cell birth, and a defect in the optokinetic response. The mechanistic link between high glucose and changes in retinal development is not well described but may involve an increase in reactive oxygen species.
Major comments:
- Is the photoreceptor phenotype a degenerative rather a developmental phenotype? In embryos treated with high glucose, photoreceptors in the periphery of the retina near the ciliary margin, which are younger in age, seem to be structurally more normal than those at the center, away from the ciliary margin, which are older in age. Could this reflect the fact that photoreceptor development proceeds normally followed by degenerative changes?
- For many or most phenotypes the main examined treatment is glucose + dexamethasone. The authors state this combination achieves more uniform glucose concentrations in the embryos as compared to glucose alone. However, dexamethasone may have effects independently of glucose and the dexamethasone only control is not used in some or most experiments. For example in Fig. 3, could dexamethasone alone causes changes in photoreceptor morphology? In the combo treatment, is it possible that some effects are simply due to a synergism of glucose+dex and not because dex causes a more uniformly high intraembryonic glucose?
- It is interesting that hyperglycemic retinas show more neurons born between 2-5 days post fertilization in the RGC layer than in the outer nuclear layer (Fig 7). One interpretation is delayed birth of RGCs after hyperglycemia as the authors suggest. Another interpretation is that non-RGC cell types are in now in the RGC layer; or that some proliferating progenitors persist at 5dpf. Co-localization of EdU with differentiation markers, and EdU analysis after a short pulse of 2 hours would help to nail down if there is developmental delay or something else going on here.
- Do Müller cells go into cycle after high glucose treatment?
- The increase in ROS in Fig. 6 does not seem very convincing. Is the difference between untreated and glucose or glucose/dex treatments statistically significant? I would avoid making too much of this unless some type of phenotype rescue with N-acetylcysteine or vitamin C, or Trolox, can be shown. Methylene blue is a bit non-specific as an antioxidant.
Significance
The translational significance of the findings is that they might provide a model to study how embryonic hyperglycemia due to maternal diabetes changes embryonic development. Pitfalls include the fact that its relevance to humans is unclear. Is maternal diabetes known to cause visual abnormalities due to abnormal retinal development in newborns? The basic biology significance may be to provide a model to investigate how glucose metabolism is connected to developmental decisions. However it is unclear whether glucose metabolism within retinal cells mediates the observed effects; and the high glucose used here is likely unphysiological as at these developmental stages zebrafish embryos feed from the yolk sac.
Audience interested in this work may include zebrafish developmental biologists. My expertise: metabolism, retinal development.
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Referee #1
Evidence, reproducibility and clarity
Summary
In this work, the authors Titialii-Torres and Morris assess how hypergycemia affects the development of the neural retina using a genetic and a nutritional approach in the model organism zebrafish. This is important as diabetes can contribute to retinal degeneration in during the progression of diabetic retinopathy which often leads to blindness in adults.
The authors examine how different cell types in the neural retina are affected in a genetic hyperglycemic model, the pdx1 mutant embryos, and in a nutritional model, in which hyperglycemia is induced by glucose and dexamethasone exposure. Titialii-Torres and Morris show that in both models, photoreceptor rods and cones, as well as horizontal cells, are reduced in number. Additionally, they report a delay in retinal cell differentiation accompanied by increased ROS production in the hyperglycemic retina. Altered expression of metabolism related genes and effects on visual function were also found in their hyperglycemic models. Overall, the assessment of the different retinal cell types impacted by hyperglycemia and examination of potential molecular mechanisms contributes important and novel data to the field. However, the data as presented falls short in supporting the conclusions of the authors.
Major comments
Overall, the conclusions would be more strongly supported by improving the clarity of the images, and by additional analyses.
Figure1:
o Referring to figure 1 E' the text states that an arrowhead points to the shorter and thinner outer segment of a rod. In the figure there is an arrow pointing to a cell without a visible outer segment, making it hard to make the same conclusion.
o Additionally the GFP signal is very weak in D and E in the dorsal retina. Therefore it is not possible to see if there is also a decreased amount of rods in the dorsal retina as claimed.
o In the text it is mentioned that cones in the ventral region are affected. Is there also a difference in the dorsal region?
Figure 3:
o Rods and cones might be better displayed in close-ups from sections rather than from projections of the whole eye.
o The authors write about a reduction of cones upon glucose treatment. In the graph this is not highlighted as significant.
Figure 4: as the overall number of cones was already assessed before, focusing on a smaller region might help the reader to see the Zpr3 staining showing that the outer segments of the cones are stunted (as stated in the main text). In the figure panels presented, outer segments cannot be clearly seen.
Figure 6: scale bar is missing. Please clarify what the red and the green is. Why is there a red signal from Mitosox outside of the embryo (panel C)? The fluorescence of the superoxide probe should be displayed in a more convincing way. For example, in sections to enable assignment of signal to tissues and cells, as shown in Supplemental Figure 5.
Figure 8: Is the coincubation with methylene blue leading to a significant increase in photoreceptors? If yes, this should be indicated in the graph.
Supplemental Figure 2: The authors assert that TUNEL+ cell labeling coincides with Müller glial cells. This would be better supported with a magnified view of the INL, optimally by applying TUNEL staining to hyperglycemic, GFAP:GFP transgenic samples.
It would be of interest to determine if an incubation with methylene blue also affects photoreceptors in pdx1 mutants. Is it possible to confirm that Methylene blue treatment reduces ROS in the retina ? Can changes in ROS response gene expression be demonstrated by qPCR ? The assumptions about ROS should be either strengthened by additional experiments or less emphasized in the discussion.
For completeness, glucose metabolism in the genetic model should be also addressed and compared to the nutritional model.
The authors talk about a "long term" return to normoglycemia and long term effects of hyperglycemia. Analysis at 7 dpf after a 2 day return to normoglycemic conditions can hardly be called long term. To make these statements, an assessment after a longer time period (one week or more if possible?) would be more convincing.
The claims of 'reactive gliosis' in glucose-treated larvae is overstated. Biologically meaningful differences in cell shape between control and treated samples are not evident from the images (Fig. 5A-F). This should at least be quantitated by shape analysis. The Glucose+Dex samples do not show increased number of Müller glial cells, and glucose treatment alone leads to highly variable glucose levels. This complicates and weakens a correlation with hyperglycemia.
In addition, there are many minor inconsistencies and awkwardness in the presentation of the figures, as detailed below.
Minor comments
Some figures would benefit if they would follow the sequence of the text. Eg: figure 1 and 3, the text addresses first the rods and then the cones.
In several places the panels referred to in the text do not match the figures or figure panels are not mentioned at all. For example:
Pg 3 "Quantification revealed a significant decrease in both rod and cone photoreceptors in pdx1 mutants at 5 dpf (Fig. 1C)."
- the quantification is in panels C and F.
The main text does not mention or explain Figure 2A Pg 5 "The results confirmed that rods and cones from hyperglycemic larvae have shorter outer segments compared to wild type larvae at 5 dpf (Fig. 4A-C)."
- panel C is a graph of Saccades.
Fig. S3 - only panel Y is referred to in the text.
Supplemental figure 2: the authors claim a significant increase of apoptotic cells in the genetic model. In the corresponding graph significance is not indicated.
Figure 5: scale bars are missing, the figure text and the numbering of the figure do not fit.
Supplemental figures 4 and 5:
o The Prox1 staining is hard to see and it is unclear what was counted as cells.
o In Supp Fig. 4E the PKC staining looks increased compared to the controls.
o The graphs could have similar y axes, especially because in supplemental figure 5 the amount of cells/µm is also different. Why not always use per 50µm? Shouldn't the amount of cells in wild types and untreated embryos be the same per 50µm?
o Also the labelling of the y axes could be made coherent in the two figures.
Supplemental figure 6: K is not mentioned in the legend.
2-NDBG treatment is not explained in material and methods
Significance
Significance
Titialii-Torres et al. characterize the impaired development of neural retinal cells under hyperglycemic conditions in zebrafish larvae and also show evidence of impaired visual function. This work will be of interest for researchers in the field of diabetes, especially those focused on diabetic retinopathy, and for developmental biologists interested in pathologies that impact human development. While the manuscript provides insights into the development of the retina under hyperglycemic conditions, a revision addressing weaknesses of figure presentation and some additional confirmatory experiments would be of great benefit.
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Transparent Peer Review
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Reply to the reviewers
The authors do not wish to provide a response at this time.
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Referee #2
Evidence, reproducibility and clarity
Kleijn et al. measured transcript and protein abundance in fission yeast cultures growing on different nutrient sources (and thus at different growth rates) in turbidostats. Their experimental design is sound and the data quality appears good. The authors focus on analyzing their data from the vantage point of previously reported ideas on principles of proteome allocation, and expand beyond this framework with interesting analyses, e.g., on the stoichiometry of translation complexes changes with the growth rate.
Generally I find the paper well written and the conclusions well substantiated. Below are specific recommendations that may help the authors improve their study:
- Your data allow investigating the extend of transcriptional and post-transcriptional regulation in fission yeast, and I think this analysis will be very interesting. PMID: 28481885 provides one simple approach to such analysis, and the authors may use another. Importantly, they authors must account for measurement noise.
- Your analysis of the ribosomal proteins (RP), the ribosome biogenesis regulon (RiBi), and the translation initiation, elongation and termination factors (IET) is interesting. I would love to know whether there changes within these groups of proteins, e.g., different RP in budding yeast change differently with growth rate (PMID: 24767987, PMID: 26565899) and I would love to know if this is the case with fission yeast.
- The Z score ranges on some of the heatmaps (e.g. fig 2A) are so wide that the changes in protein / RNA abundance are difficult to see.
- It will be very useful to perform unbiased gene set enrichment analysis of the functions that show significant growth rate dependent and nutrient dependent effects, e.g., as in Fig 11 of PMID: 21525243
Significance
I am an expert in this field, and I think that this study represents a significant advance.
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Referee #1
Evidence, reproducibility and clarity
In this paper Kleijn et al study global gene expression profiles in S. pombe grown in different nitrogen sources using a turbidostat that result in variation in growth rate. The authors use both RNAseq to quantify RNA expression and mass spectrometry to quantify protein expression. They find that the expression of many genes is correlated with growth rate. This finding builds on prior work performed by other groups in S. cerevisiae and bacteria that show organismal growth rate is a primary determinant of gene expression state for a large fraction of genes. The findings in this paper confirm and extend those results.
Significance
One surprising aspect of this manuscript is that the authors do not seem to have made the most of their experimental design. The acquisition of both protein and mRNA expression across these conditions provides a unique dataset for looking at how these two levels of expression agree with respect to each other. A simple plot showing the strength of the growth rate response for a gene at the level of mRNA and protein would already be interesting, but I would think that there is the opportunity to look more quantitatively at whether the ratio of mRNA to protein remains constant across growth rates or whether there systematic deviations that are biologically interesting. I would encourage the authors to address this question with their unique dataset.
Prior to publication the authors should address the following points.
At what point in the turbidostat cycle was the sampling performed? At steady state or during the dilution phase?
It is unclear in the text what transcripts are included in the category ncRNA. Does this include tRNA and rRNA?
The basis for the abbreviations for positive (R) negative (P) and not significant (Q) are obscure. Why not P, N, NS?
In Brauer et al., the fraction of cells in G1 is correlated with growth rate. Is that the case in S pombe? Is there any relationship between cell cycle gene expression and growth rate related gene expression?
Is there anything unique to the set of ~100 genes that are anticorrelated between mRNA and protein in response to growth rate variation?
A clearer explanation of the FC metric and the rationale for its use should be made in the results. What is FC an abbreviation for? It is unclear why this metric is needed, when the strength of the response to growth rate is captured by the slope.
Airoldi et al., 2016 and Airoldi et al., 2009 looked at methods for normalizing gene expression to growth rate and may be relevant sources.
The contrast in the experimental rationale between using chemostats and turbidostats is interesting, but I am left unclear about whether the result is really that different. What is the key distinction in the observed data in comparing gene expression response to growth rate in the chemostat and turidostat?
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity (Required)): In this manuscript, using in vivo infection of Zebrafish embryos with Mycobacterium marinum and THP1-derived macrophages infected with Mycobacterium tuberculosis, the authors show that these pathogenic mycobacteria trigger an increase of K+ concentration through the expression of OXSR1. The ESX1 secretion system that is essential for the virulence of M. marinum is required for the expression of OXSR1 and SPAK. OXSR1 and SPAK are involved in the WNK signaling pathway and are cytoplasmic serine/threonine protein kinases that regulate the function of a series of sodium, potassium and chloride co-transporters via phosphorylation. Given that K+ efflux is now accepted as the main inducer of NLRP3 inflammasome, the authors report that this infection-induced OXSR1 expression restrains the protective NLRP3 inflammasome response leading to IL-1b maturation and secretion. Il-1b as a very potent pro-inflammatory triggers TNF-a production and the authors demonstrate that infection-induced OXSR1 expression suppressed host protective TNF-a and cell death early in fection. It appears therefore that virulent mycobacteria induce OXSR1 expression to reduce inflammasome activation by maintaining high intracellular K+. The results presented by the authors are convincing and the conclusions raised by the authors are well supported by the data. In zebrafish embryos, OXSR1 knockdown nicely reduces mycobacteria burden. Based on their conclusions that infection-induced OXSR1 expression reduces NLRP3 inflammasome activation, NLRP3 inflammasome activation has therefore a protective effect against bacterial infection. My main concern is that surprisingly, nlrp3 or il1b knockdown has no effect on bacterial burden in comparison to control embryos. Lane 256, as an explanation, the authors wrote "This may have been because we were using mosaic F0 CRISPR knockout, which is not a complete removal". The removal using mosaic F0 CRISPR knockout is nevertheless sufficient to observe a decrease in bacterial burden following OXSR1 knockdown. Would it be possible that OXSR1 also regulates immunity independently of NLRP3 inflammasome?
Yes, we will add text to the discussion to address potential NLRP3-independent mechanisms that connect OXSR1 to immunity against mycobacterial infection.
The lack of effect of il1b knockdown on M. marinum burden has been corroborated by independent laboratories including a publication from the Elks lab in Journal of Immunology: Ogryzko et al 2019. The Ogryzko study found no effect of il1b knockout on M. marinum burden.
**Other comments:** OXSR1 WB in extended Data 3 is really poor quality so that it is hard to see the increased expression of OXSR1 following infection.
The western blot will be repeated for cleaner images.
Figure 2C. It is not shown but I guess that similar results should be obtain using M. tuberculosis.
Material leaving our BSL3 facility must be decontaminated which makes this suggested analysis impossible in our facility.
Figures 5D and 5E. To confirm the involvement of NLRP3, in addition of using MCC950, NLRP3 knock down using siRNA should be also performed. NLRP3-deficient THP-1 cells are also commercially available if the siRNA-mediated knock down of NLRP3 is not convincing enough.
We will purchase NLRP3 deficient THP-1 cells and use our existing shRNA vector to create NLRP3 and OXSR1 deficient cells. We will repeat the experiments in 5D and 5E in these cells to confirm NLRP3 involvement.
**Minor comments:** How do the authors think that mycobacterium induces OXSR1 expression following infection? It has not been investigated and it is not discussed.
In Fig1A we showed upregulation of oxsr1a transcription and in Fig2A we showed upregulation of OXSR1 protein. In line 204 of the discussion we described our hypothesis that oxsr1a transcription is responsive to the mycobacterial ESX1 secretion system.*
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Reviewer #1 (Significance (Required)): The observations reported in this manuscript are interesting since for the first time, it is described that virulent mycobacteria induce OXSR1 expression to reduce NLRP3 inflammasome activation by maintaining high intracellular K+. This is quite a significant advance in the field. To escape immune control, many successful intracellular pathogens have evolved methods to limit inflammasome activation. While it is known that potassium efflux is a trigger for inflammasome activation, the interaction between mycobacterial infection, potassium efflux and inflammasome activation was not explored. My field of expertise is the regulation of inflammasome activation. As far as I remember, I've never reviewed a paper using zebrafish embryos but here, the explanations and data are clear so that it was easy to understand and to evaluate. Likewise, I did not know the WNK signaling pathway but the literature clearly shows that it is involved in intracellular ionic balance.
Reviewer #2 (Evidence, reproducibility and clarity (Required)): Hortle et al, in this study evaluated the role of WNK kinases SPAK and OXSR1 during M. marinum and M. tuberculosis infection. These two kinases inhibit the KCC channels which have a tendency to export potassium out of the cell. Since potassium efflux is a known stimulator of NLRP3 inflammasome activation, this raises the possible role of these kinases in inflammation and infection. Authors showed that inhibiting OXSR1 genetically and chemically reduced the mycobacterium survival in cells and zebrafish model, thus proposing OXSR1 as a host-directed therapeutic candidate. They showed that knockdown of OXSR1a leads to NLRP3 inflammasome mediated IL1B induction, which results in increase in TNFa and suppression of mycobacterium growth. Furthermore, reduction in mycobacterium growth in OXSR1a KD zebrafish embryos was found to be dependent on ESX1 machinery of Mycobacterium. The role of potassium in regulating Mycobacterium host response is novel. However there are few things which are missing from this interesting work. **Main comments**
- Since OXSR1 is known to inhibit KCC channels, which will lead to increase intracellular potassium. Why in infected control cells there is no increase potassium, Fig 2C. What would be the role of potassium in OXSR1 mediated control of Mtb growth?
We will perform more experiments with altered levels of extracellular potassium to determine if infected control cells have increased intracellular potassium compared to OXSR1 knockdown cells.
Does addition of extracellular potassium restricts mycobacterium in OXSR1-KD cells?
We will perform additional experiments with the addition of potassium to the cell culture medium to address this concern.
Since OXSR1 is known to inhibit KCC channels, What happens to the activity of these channels in OXSR1 KD cells? This is important, because authors could not find any difference in intracellular potassium between uninfected control and uninfected OXSR1 KD cells (Fig 2C). It will be good to add the flowcytometric histogram or dot plots of potassium staining in the main figure or in extended figures.
We have data showing that although there is minimal difference in basal K+ level in OXSR1 KD cells, there is significantly lower K+ level when the cells are placed in High K+ media, or osmotic shock. We will include this data in the revised manuscript. We will amend the figures to include Flow plots.
Acquisition of potassium stained cells - In methodology it has been mentioned that ion K+ Green stained undifferentiated THP1 cells were acquired using PE channel while differentiated THP1 cells were acquired using FITC channel. Furthermore in methods its mentioned that Leica Sp8 microscope was used to acquire images, however I do not see any of this data in the manuscript.
Ion K+ green emits into both the PE and FITC channels. Our choice to use the FITC or PE channel depended on whether the cells were also infected with red fluorescent bacteria which “contaminates” the PE channel.
Fig 2E and 3D - Meaning of "Normalized CFU/ml"? Each dot represents what? How many times this experiment was performed, please add in the legend.
Normalized CFU/ml means that the CFU at 3 day post infection were normalized to the 0 day post infection intracellular bacterial burden, to adjust for any differences in phagocytosis of bacteria. Each dot represents the CFU from an infected well in a single representative experiment and the experiment was repeated 3 times. This information will be added to the figure legend.
Fig 1D - What could be the reason of no statistical significant difference between wild type and homozygous oxsr1a-KO fish?
This data is from two experimental replicates. We are currently growing more breeding fish to generate embryos for experimental replicates.
Good to have a schematic model showing the finding s of the study
We will add a schematic model to the manuscript.
TNFa is double edge sword and can lead to pathology. Hence treatment of chronically infected animals (say mice) by Compound B, will be needed to confirm the HDT activity of OXSR1.
Yes, we will add discussion of this point as a caveat to our future direction of using OXSR1 inhibition as a HDT.
Reviewer #2 (Significance (Required)): This study showed role of kinases, which regulate trafficking of potassium, in mycobacterium-host interaction. Since kinases are draggable, so this opens a new area for developing host-directed therapies for TB. Reviewer #3 (Evidence, reproducibility and clarity (Required)): In this study, the authors suggest to have evidence for OXSR1 to inhibit NLRP3 inflammasome activation by limiting potassium efflux during mycobacterial infection. To my opinion, the study lacks important results supporting their main conclusions. In many instances, the authors have over-interpreted their data and I therefore do not support publication of this study. **Main comments:** Activation of the NLRP3 inflammasome upon OXSR1 knockdown was not convincingly demonstrated.
We will address the activation state of the NLRP3 inflammasome with NLRP3 KO and OXSR1 KD cells as also suggested by reviewer 1: We will purchase NLRP3 deficient THP-1 cells and use our existing shRNA vector to create NLRP3 and OXSR1 deficient cells. We will repeat the experiments in 5D and 5E in these cells to confirm NLRP3 involvement.
Clearance of bacteria in an organism, herein zebrafish, involves mechanisms in different cell types including downstream of inflammasome activation. Thus, bacterial clearance experiments in THP-1 cells might not necessarily be related to in vivo experiments in an organismal context. Finally, a mechanism as to how mycobacteria enhance OXSR1 expression to block a NLRP3-mediated response has not been addressed.
We are not able to perform in depth analysis of the bacterial side of this host-pathogen interaction as my lab will close in the next 4 months. We have shown that transcriptional upregulation of oxsr1a is ESX1-dependent. We will include data on OXSR1 protein expression with WT and ESX1 mutant bacteria when we repeat the western blots in Extended data 3.
**Specific comments:**
- The author showed that the M. marinum ESX1 secretion system induced OXSR1 expression to inhibit the NLRP3 inflammasome activation. This is contradictory to another recent study (PMID: 18852239), which showed that the ESX1 secretion system activated the NLRP3 inflammasome. These effects are not mutually exclusive. The ESX1 secretion system has a “deliberate” purpose in exporting mycobacterial effector proteins to subvert cellular immunity while also having an “accidental” role in exposing the host cell cytosol to vacluolar contents that can activate cellular immunity. We do not assert that mycobacteria completely inhibit all NLRP3 activation – rather that attempts to stop full activation via inducing the expression of host OXSR1. This can be seen in the IL-1b data in figure 3E, where infected WT cells release more IL-1b than MCC950 treated cells, but less than OXSR1 KD cells.
In line 102, based on Data shown in Fig 1D, the authors concluded that homozygous, but not heterozygous, oxsr1asyd5 embryos showed reduced bacterial burden. However, in Fig 1D, the difference among the genotypes is not significant.
This concern will be addressed with additional replicates.
In line 196, the authors stated that "We present evidence that pathogenic mycobacteria increase macrophage K+ concentration by inducing expression of OXSR1." However, the authors did not provide evidence for this.
We will soften this phrase in the discussion to replace “by inducing” with “and induce”.
Based on Extended data 3, the authors concluded that infection increases the expression of OXSR1. However, this is not evidenced in the Western Blot. In addition, in panel B, the OXSR1 blot showed many non-specific bands with decreased intensity in OXSR1 knockdown conditions suggesting that there is unequal protein loading making it impossible to interpret these results.
We will repeat the western blots as per Reviewer 1’s comment as well.
The authors concluded that infection-induced OXSR1 expression suppressed inflammasome activity to aid mycobacterial infection. Experiments with Compound B, that inhibits OXSR1 phosphorylation, are used in support of the above conclusion. I do not really see a connection between OXSR1 expression and the inhibitor experiment.
We will reword “expression” to “activity” in regards to the inhibitor experiment.
In line 187, "Knockdown of tnfa reduced the amount of infection-induced tnfa promoter-driven GFP produced around sites of infection ....". How can a knockdown of tnfa affect the GFP expression driven by the tnfa promoter ?
The promoter fragment used in the TgBAC construct contains target sites for two of our guide RNAs. We will also include qPCR validation of the knockdown.
Reviewer #3 (Significance (Required)): Mechanism underlying decreased intracellular potassium level is of great interest in the inflammasome field. However, their observation is not in line with published studies. Audience in the pathogen-host interaction field will be interested. Expertise: dissection of signalling pathway regulation, molecular and cellular mechanism underlying NLRP3 inflammasome activation. We are not using zebrafish model.
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Referee #3
Evidence, reproducibility and clarity
In this study, the authors suggest to have evidence for OXSR1 to inhibit NLRP3 inflammasome activation by limiting potassium efflux during mycobacterial infection. To my opinion, the study lacks important results supporting their main conclusions. In many instances, the authors have over-interpreted their data and I therefore do not support publication of this study.
Main comments:
Activation of the NLRP3 inflammasome upon OXSR1 knockdown was not convincingly demonstrated. Clearance of bacteria in an organism, herein zebrafish, involves mechanisms in different cell types including downstream of inflammasome activation. Thus, bacterial clearance experiments in THP-1 cells might not necessarily be related to in vivo experiments in an organismal context. Finally, a mechanism as to how mycobacteria enhance OXSR1 expression to block a NLRP3-mediated response has not been addressed.
Specific comments:
- The author showed that the M. marinum ESX1 secretion system induced OXSR1 expression to inhibit the NLRP3 inflammasome activation. This is contradictory to another recent study (PMID: 18852239), which showed that the ESX1 secretion system activated the NLRP3 inflammasome.
- In line 102, based on Data shown in Fig 1D, the authors concluded that homozygous, but not heterozygous, oxsr1asyd5 embryos showed reduced bacterial burden. However, in Fig 1D, the difference among the genotypes is not significant.
- In line 196, the authors stated that "We present evidence that pathogenic mycobacteria increase macrophage K+ concentration by inducing expression of OXSR1." However, the authors did not provide evidence for this.
- Based on Extended data 3, the authors concluded that infection increases the expression of OXSR1. However, this is not evidenced in the Western Blot. In addition, in panel B, the OXSR1 blot showed many non-specific bands with decreased intensity in OXSR1 knockdown conditions suggesting that there is unequal protein loading making it impossible to interpret these results.
- The authors concluded that infection-induced OXSR1 expression suppressed inflammasome activity to aid mycobacterial infection. Experiments with Compound B, that inhibits OXSR1 phosphorylation, are used in support of the above conclusion. I do not really see a connection between OXSR1 expression and the inhibitor experiment.
- In line 187, "Knockdown of tnfa reduced the amount of infection-induced tnfa promoter-driven GFP produced around sites of infection ....". How can a knockdown of tnfa affect the GFP expression driven by the tnfa promoter ?
Significance
Mechanism underlying decreased intracellular potassium level is of great interest in the inflammasome field. However, their observation is not in line with published studies.
Audience in the pathogen-host interaction field will be interested.
Expertise: dissection of signalling pathway regulation, molecular and cellular mechanism underlying NLRP3 inflammasome activation. We are not using zebrafish model.
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Referee #2
Evidence, reproducibility and clarity
Hortle et al, in this study evaluated the role of WNK kinases SPAK and OXSR1 during M. marinum and M. tuberculosis infection. These two kinases inhibit the KCC channels which have a tendency to export potassium out of the cell. Since potassium efflux is a known stimulator of NLRP3 inflammasome activation, this raises the possible role of these kinases in inflammation and infection. Authors showed that inhibiting OXSR1 genetically and chemically reduced the mycobacterium survival in cells and zebrafish model, thus proposing OXSR1 as a host-directed therapeutic candidate. They showed that knockdown of OXSR1a leads to NLRP3 inflammasome mediated IL1B induction, which results in increase in TNFa and suppression of mycobacterium growth. Furthermore, reduction in mycobacterium growth in OXSR1a KD zebrafish embryos was found to be dependent on ESX1 machinery of Mycobacterium.
The role of potassium in regulating Mycobacterium host response is novel. However there are few things which are missing from this interesting work.
Main comments
- Since OXSR1 is known to inhibit KCC channels, which will lead to increase intracellular potassium. Why in infected control cells there is no increase potassium, Fig 2C. What would be the role of potassium in OXSR1 mediated control of Mtb growth? Does addition of extracellular potassium restricts mycobacterium in OXSR1-KD cells?
- Since OXSR1 is known to inhibit KCC channels, What happens to the activity of these channels in OXSR1 KD cells? This is important, because authors could not find any difference in intracellular potassium between uninfected control and uninfected OXSR1 KD cells (Fig 2C). It will be good to add the flowcytometric histogram or dot plots of potassium staining in the main figure or in extended figures.
- Acquisition of potassium stained cells - In methodology it has been mentioned that ion K+ Green stained undifferentiated THP1 cells were acquired using PE channel while differentiated THP1 cells were acquired using FITC channel. Furthermore in methods its mentioned that Leica Sp8 microscope was used to acquire images, however I do not see any of this data in the manuscript.
- Fig 2E and 3D - Meaning of "Normalized CFU/ml"? Each dot represents what? How many times this experiment was performed, please add in the legend.
- Fig 1D - What could be the reason of no statistical significant difference between wild type and homozygous oxsr1a-KO fish?
- Good to have a schematic model showing the finding s of the study
- TNFa is double edge sword and can lead to pathology. Hence treatment of chronically infected animals (say mice) by Compound B, will be needed to confirm the HDT activity of OXSR1.
Significance
This study showed role of kinases, which regulate trafficking of potassium, in mycobacterium-host interaction. Since kinases are draggable, so this opens a new area for developing host-directed therapies for TB.
-
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Referee #1
Evidence, reproducibility and clarity
In this manuscript, using in vivo infection of Zebrafish embryos with Mycobacterium marinum and THP1-derived macrophages infected with Mycobacterium tuberculosis, the authors show that these pathogenic mycobacteria trigger an increase of K+ concentration through the expression of OXSR1. The ESX1 secretion system that is essential for the virulence of M. marinum is required for the expression of OXSR1 and SPAK. OXSR1 and SPAK are involved in the WNK signaling pathway and are cytoplasmic serine/threonine protein kinases that regulate the function of a series of sodium, potassium and chloride co-transporters via phosphorylation. Given that K+ efflux is now accepted as the main inducer of NLRP3 inflammasome, the authors report that this infection-induced OXSR1 expression restrains the protective NLRP3 inflammasome response leading to IL-1b maturation and secretion. Il-1b as a very potent pro-inflammatory triggers TNF-a production and the authors demonstrate that infection-induced OXSR1 expression suppressed host protective TNF-a and cell death early in fection. It appears therefore that virulent mycobacteria induce OXSR1 expression to reduce inflammasome activation by maintaining high intracellular K+.
The results presented by the authors are convincing and the conclusions raised by the authors are well supported by the data.
In zebrafish embryos, OXSR1 knockdown nicely reduces mycobacteria burden. Based on their conclusions that infection-induced OXSR1 expression reduces NLRP3 inflammasome activation, NLRP3 inflammasome activation has therefore a protective effect against bacterial infection. My main concern is that surprisingly, nlrp3 or il1b knockdown has no effect on bacterial burden in comparison to control embryos. Lane 256, as an explanation, the authors wrote "This may have been because we were using mosaic F0 CRISPR knockout, which is not a complete removal". The removal using mosaic F0 CRISPR knockout is nevertheless sufficient to observe a decrease in bacterial burden following OXSR1 knockdown. Would it be possible that OXSR1 also regulates immunity independently of NLRP3 inflammasome?
Other comments:
OXSR1 WB in extended Data 3 is really poor quality so that it is hard to see the increased expression of OXSR1 following infection.
Figure 2C. It is not shown but I guess that similar results should be obtain using M. tuberculosis.
Figures 5D and 5E. To confirm the involvement of NLRP3, in addition of using MCC950, NLRP3 knock down using siRNA should be also performed. NLRP3-deficient THP-1 cells are also commercially available if the siRNA-mediated knock down of NLRP3 is not convincing enough.
Minor comments:
How do the authors think that mycobacterium induces OXSR1 expression following infection? It has not been investigated and it is not discussed.
Significance
The observations reported in this manuscript are interesting since for the first time, it is described that virulent mycobacteria induce OXSR1 expression to reduce NLRP3 inflammasome activation by maintaining high intracellular K+. This is quite a significant advance in the field. To escape immune control, many successful intracellular pathogens have evolved methods to limit inflammasome activation. While it is known that potassium efflux is a trigger for inflammasome activation, the interaction between mycobacterial infection, potassium efflux and inflammasome activation was not explored.
My field of expertise is the regulation of inflammasome activation. As far as I remember, I've never reviewed a paper using zebrafish embryos but here, the explanations and data are clear so that it was easy to understand and to evaluate. Likewise, I did not know the WNK signaling pathway but the literature clearly shows that it is involved in intracellular ionic balance.
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity (Required):
In this project, authors develop a colorimetric and luminescence assay for the detection of SARS-CoV-2 RNA in vitro. They design an RNA based sensor that will be triggered by target RNA then release the ribosome binding site and a translation start site followed by a reporter gene. The released sequence will then trigger the production of reporter protein by transcription-translation coupled assay. Authors also introduce an RNA amplification step in order to increase the sensitivity of this assay.
**Strengths:**
This assay provides a simple, rapid way to detect SARS-CoV2 and it is an elegant way to incorporate transcription-translation coupled assay for SARS-CoV-2 RNA detection and identify SARS-CoV-2 patient samples. It is a nice assay and the performance is comparable with the existing method.
**Weaknesses:**
However, the positioning of this assay is not very clear. The readout of this assay could be recorded by camera whereas it includes several steps such as RNA extraction, amplification, transcription-translation coupled assay and reporter reaction. The limitations of the existing methods (RT-PCR, paper strip) and the advantages of this assay haven't been demonstrated by the experiments. The stability of RNA may also restrict the application of the proposed assay on site.
**Major comments:**
Authors are suggested to design an experiment to show the advantage of this assay compared with the existing method.
Response: We thank the reviewer for pointing this out. In Fig 5, we show a comparison of our assay with the bench mark in COVID-19 diagnostics, which is the RT-qPCR assay. We specifically correlate the Ct- values obtained for RT-qPCRs with the amount of color or luminescence obtained through our assay. From these experiments we note that the sensitivity of our assay is a lttle less than the RT-qPCRs where our assay does not detect Ct-values in the 36 to 38 range (very low viral loads). This comparative experiment highlights that our assay bears clear advantages over the RT-qPCR in terms of ease of assay set up, ease of color detection, amenability to cell-phone imaging and no requirement of sophisticated equipment or technical training to interpret results. The full details of these comparisons are discussed in the manuscript.
This is consistent with the literature on COVID-19 diagnostics where new assays are routinely bench-marked against the “gold-standard” RT-qPCR assay ((Corman et al., 2020; Pearson et al., 2021).
What is the limit of detection of this assay using LacZ and Luciferase reporter respectively?
Response: The limit of detection of the assay as shown in Fig 4B and Fig 4C-D, was found to be 100 copies of RNA, which translates to a concentration of 8 attomolar RNA. In this case, we find the limit of detection to be the same for both LacZ (Fig 4B) and Luciferase (Fig 4C-D) reporter.
The calculations of copy number and sensitivity were made using a commercial source of synthetic CoV-2 RNA (Twist Biosciences) that is used in several studies about COVID-19 diagnostics (Joung et al., 2020; Rabe & Cepko, 2020; Wu et al., 2021). The RNA copy numbers are taken from the product details provided by the manufacturer. These details are now clearly stated in the manuscript. The commercial RNA is provided at 106 copies per ul. From this we take as low as 100 copies per 20ul of NASBA reaction, which we are able to detect using our assay. Hence our sensitivity comes to 8 attoMolar. We have clarified this in the manuscript. We noticed a typo in the original submission where we refer to a sensitivity of 80 attomolar in the Discussion. This is corrected to 8 attomolar. With this sensitivity we are within the range to detect RNA in patient samples, as confirmed by our patient data.
Authors have not examined the selectivity of this assay. What is the specificity, selectivity for each of these variants? Does altering target RNA change the specificity?
Response: We thank the reviewer for raising this point. As recommended by the reviewer, we have now examined the selectivity of this assay through new data (See new Fig S3, new Fig S4 and new Fig S8, also shown below).
We have examined selectivity in 3 different ways.
- Is our sensor selective to the said region of the SARS-CoV-2 genome? To address this, we generated 19 different Target (Trigger) RNAs spread across the SARS-CoV-2 genome. These were tested against Sensor 12 to examine for their ability to trigger the sensor. We find that our sensor is highly selective for its target RNA and does not show any detectable response to the other regions of SARS-CoV-2 (see new Fig S3).
Next, we asked if our assay is selective to SARS-CoV-2 versus other related human corona viruses. For this, we first examined the sequence of the target RNA (Amplicon RNA 12) that is sensed by Sensor 12. We selected equivalent regions of RNA from a different coronavirus, the HKU1 human coronavirus family. We generated these RNA sequences in vitro and performed IVTT. These new data are shown in new Fig S4 and below. We find that the human coronavirus (HKU1) RNAs are not able to turn on our sensor, whereas the cognate SARS-CoV-2 RNA is able to.
We then asked if our assay can detect a current prominent variant of SARS-CoV-2. A major cause of concern is the ability of SARS-CoV-2 to accumulate mutations in its genome, resulting in different variant strains of SARS-CoV-2. Of these variants, the Delta variant (B.1.617.2) is not only highly contagious but has been noted as a possible vaccine breakthrough mutant of SARS-CoV-2. For this, we obtained RNA from the patient nasopharyngeal swab samples from the NCBS-inStem Covid-19 testing Center, Bangalore, India. RNA was isolated in the BSL-3 facility at the testing center. RNA samples were sequenced and confirmed to be the Delta variant- B.1.617.2 (sequences deposited in GASIAD). RNA extracted from these patient samples were tested against Sensor 12 using NASBA followed by IVTT. We find that our assay can efficiently detect the Delta variant SARS-CoV-2 RNA from patient samples with a build up of color, but no color was observed from control samples. These new data are shown below and in new Fig 5F and new Fig S8. The ability to detect the Delta variant of SARS-CoV-2 is an important feature of our sensor since this variant is now of global concern and extensively found in the population, even becoming the dominant variant in several countries (Callaway, 2021; O’Dowd, 2021; Torjesen, 2021).
In Figure 2C-F, sensor 17 showed higher fold change and sensitivity. Why was sensor 12 selected for further study in Figure 3
Response: The reviewer rightly notes that sensor 17 responds to 1012 copies of RNA and hence appears to be inherently more sensitive than sensor 12, which responds to 1013 copies of RNA. However, neither of these sensitivities are good enough to detect the levels of viral RNA found in patient samples. Hence we coupled these sensors with a step of NASBA amplification. The screen to identify pairs of NASBA primers gave us great hits for sensor 12 right off the bat, where we could detect down to 100 copies of RNA. Hence we moved forward with sensor 12 for further experiments. This has now been clarified in the manuscript.
Authors should show the error bar in all plots. Authors should also indicate what the error bar means (SD, S.E.M. etc.) throughout the manuscript.
Response: This is an important point. We have added the error bars and statistical analyses to all relevant plots. We have included the description of these statistical parameters in the figure legends throughout the manuscript, where relevant. Alternatively, experimental replicates are indicated and shown in the revised manuscript. Specifically in Figures 2 and 3 and 4D we have performed statistical analysis to include p-values to show significance of the data. For the data in Figure 4 B-C we include the experimental replicates as a new Supplementary Figure (see new Fig S5). Data in Figure S5 is now updated to include the experimental replicates. For the patient data in Figure 5, we have included details of specificity and sensitivity analysis for clinical samples (see new Fig 5C).
**Minor comments:**
"This method is relatively faster but may generate false positives due to non-specific amplification and primer interactions." Reference is needed.
Response: We have now added the following references in support of this statement. (Gadkar, Goldfarb, Gantt, & Tilley, 2018; Sahoo, Sethy, Mohapatra, & Panda, 2016)
"using the softwares Primer 3 and NUPACK." Reference is needed.
Response: We have now added the following references (Untergasser et al., 2012; Zadeh et al., 2011)
Reference 15 belongs to CRISPR-CAS based assay but it was cited under RT-LAMP assay.
Response: This has now been corrected. We thank reviewer for this.
Reviewer #1 (Significance (Required)):
This paper will be of interest to scientists interested in developing diagnostic tools for the detection of SARS-CoV2 in viral and host pathogenic sequences; genetic disorders and development of precision medicine.
Reviewer works in the field of Chemical Biology and Nanotechnology including sensor development and the application in diagnosis, cell physiological studies.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
In this manuscript, Charkravarthy et al. report a new method for detecting SARS-CoV-2 RNA in both in vitro and human saliva and nasal samples. The new detection method, PHANTOM, is capable of detecting as few as 100 copies of the SARS-CoV-2 genome. The method is demonstrated to reproducible over a large range of viral titers and results in a binary report on CoV-2 infection. From my perspective the results are strong and fairly convincing (please see comments below). There is clear, logical, flow to the experiments and engineering of the PHANTOM system. The collaborative work is well organized and logical. The work is clearly of high significance and certainly merits expedited review and publication. I would like to unambiguously state that support publication of this manuscript in its current form in the non-peer reviewed context of this journal, would be more than happy to provide further peer review of this manuscript upon submission to another journal, and would be more than happy to provide further comments if requested by the authors.
My personal background is broad in range, however, I have a long track record of research in RNA folding, structural biology, biosensor development, and bioinformatics. Given this knowledge base, I found the manuscript rather easy to read and digest. The manuscript is well written and clear. In order to expedite the process of review I will not give a detailed review which would include grammatical errors (there are are very few). Rather, I will touch on the most pressing issues I see.
**Major concerns:**
1) There a number of figures that do not show a statistical measure of significance (e.g. error bears, ANOVA, etc.). It is essential that these be included in the final peer reviewed publication. (See Figure 2A, Figure 3D, Figure 4B, Figure 4C, Figure 5A, Figure 5C, Figure 5D).
Response: This is an important point. We have added the error bars and statistical analyses to all relevant plots. We have included the description of these statistical parameters in the figure legends throughout the manuscript, where relevant. Alternately, experimental replicates are indicated.
Specifically in Figures 2 and 3 and 4D we have performed statistical analysis to include p-values to show significance of the data. For the data in Figure 4 B-C we include the experimental replicates as a new Supplementary Figure (see new Fig S5). Data in Figure S5 is now updated to include the experimental replicates. For the data in Figure 5, we have included details of specificity and sensitivity analysis for clinical samples (see new Fig 5C).
2) There are some important points that do not include references within the manuscript. I believe that the authors should reference Abdolahzadeh et al. RNA 2019 in the introduction. This manuscript describes another NASBA viral detection system using fluorescent RNA reporters (also see Trachman et al. Q. Rev. Biophys 2019, for reference on fluorescent aptamers). Also see the ROSALIND method (Jung et al. 2020 Nature Biotechnology) for detecting water contaminants using visual identification by fluorescent aptamers.
Response: We have added the above mentioned references to the manuscript as suggested by the reviewer.
3) The discussion states that "The overall sensitivity in the attomolar range ensures detection of infection in the majority of Covid-positive patients in a population". Please provide a reference to support this and explicitly state the concentration of viral RNA in patient samples. There are a number of times that the copy number of viral genomes and sensitivity of the measurement is stated throughout the manuscript. There should also be a reference and statement about concentration.
Response: The reviewer has raised multiple connected points here, which we address in the revised manuscript.
- Concentration of RNA in patient samples: We have added the references (Pujadas et al., 2020; Wyllie et al., 2020) where the authors report that the typical concentration of viral RNA in patient nasopharyngeal swab samples lies in the range of 104 to 105 copies of RNA per ml. This translates to a concentration range of 10 to 100 attoMolar. This reference is now added to the manuscript. For the patient samples used on our study, we refer to the Ct- values obtained from the RT-PCR tests and correlate Ct values to the readout from our assay, consistent with other reports on COVID-19 diagnostics ((Joung et al., 2020; Vogels et al. 2020; Wu et al., 2021).
Copy number and sensitivity: As the reviewer notes, we refer to viral genome copy number and sensitivity of our assay in the manuscript. These calculations of copy number and sensitivity were made using a commercial source of synthetic CoV-2 RNA (Twist Biosciences) that is used in several studies about COVID-19 diagnostics (Joung et al., 2020; Rabe & Cepko, 2020; Wu et al., 2021). The RNA copy numbers are taken from the product details provided by the manufacturer. These details are now clearly stated in the manuscript. The commercial RNA is provided at 106 copies per ul. From this, we take as low as 100 copies per 20ul of NASBA reaction, which we are able to detect using our assay. Hence our sensitivity comes to 8 attoMolar. We have clarified this in the manuscript. We noticed a typo in the original submission where we refer to a sensitivity of 80 attomolar in the Discussion. This is corrected to 8 attomolar. With this sensitivity we are within the range to detect RNA in patient samples, as confirmed by our patient data.
Reviewer #3 (Significance (Required)):
I think this is a significant advancement in the field. The introduction of smartphone technology to this robust diagnostic is very attractive. The work is of high significance since the researchers demonstrated robust responses against SARS-CoV-2 variants. As well all now know these are on the rise and cheap robust detection methods are essential for containing this virus.
Response: We thank the reviewers for the positive comments.
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Referee #2
Evidence, reproducibility and clarity
In this manuscript, Charkravarthy et al. report a new method for detecting SARS-CoV-2 RNA in both in vitro and human saliva and nasal samples. The new detection method, PHANTOM, is capable of detecting as few as 100 copies of the SARS-CoV-2 genome. The method is demonstrated to reproducible over a large range of viral titers and results in a binary report on CoV-2 infection. From my perspective the results are strong and fairly convincing (please see comments below). There is clear, logical, flow to the experiments and engineering of the PHANTOM system. The collaborative work is well organized and logical. The work is clearly of high significance and certainly merits expedited review and publication. I would like to unambiguously state that support publication of this manuscript in its current form in the non-peer reviewed context of this journal, would be more than happy to provide further peer review of this manuscript upon submission to another journal, and would be more than happy to provide further comments if requested by the authors.
My personal background is broad in range, however, I have a long track record of research in RNA folding, structural biology, biosensor development, and bioinformatics. Given this knowledge base, I found the manuscript rather easy to read and digest. The manuscript is well written and clear. In order to expedite the process of review I will not give a detailed review which would include grammatical errors (there are are very few). Rather, I will touch on the most pressing issues I see.
Major concerns:
1) There a number of figures that do not show a statistical measure of significance (e.g. error bears, ANOVA, etc.). It is essential that these be included in the final peer reviewed publication. (See Figure 2A, Figure 3D, Figure 4B, Figure 4C, Figure 5A, Figure 5C, Figure 5D).
2) There are some important points that do not include references within the manuscript. I believe that the authors should reference Abdolahzadeh et al. RNA 2019 in the introduction. This manuscript describes another NASBA viral detection system using fluorescent RNA reporters (also see Trachman et al. Q. Rev. Biophys 2019, for reference on fluorescent aptamers). Also see the ROSALIND method (Jung et al. 2020 Nature Biotechnology) for detecting water contaminants using visual identification by fluorescent aptamers.
3) The discussion states that "The overall sensitivity in the attomolar range ensures detection of infection in the majority of Covid-positive patients in a population". Please provide a reference to support this and explicitly state the concentration of viral RNA in patient samples. There are number of times that the copy number of viral genomes and sensitivity of the measurement is stated throughout the manuscript. There should also be a reference and statement about concentration.
Significance
I think this is a significant advancement in the field. The introduction of smart phone technology to this robust diagnostic is very attractive. The work is of high significance since the researchers demonstrated robust reposes against SARS-CoV-2 variants. As well all now know these are on the rise and cheap robust detection methods are essential for containing this virus.
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Referee #1
Evidence, reproducibility and clarity
In this project, authors develop a colorimetric and luminescence assay for the detection of SARS-CoV-2 RNA in vitro. They design an RNA based sensor that will be triggered by target RNA then release the ribosome binding site and a translation start site followed by a reporter gene. The released sequence will then trigger the production of reporter protein by transcription-translation coupled assay. Authors also introduce an RNA amplification step in order to increase the sensitivity of this assay.
Strengths:
This assay provides a simple, rapid way to detect SARS-CoV2 and it is an elegant way to incorporate transcription-translation coupled assay for SARS-CoV-2 RNA detection and identify SARS-CoV-2 patient samples. It is a nice assay and the performance is comparable with the existing method.
Weaknesses:
However, the positioning of this assay is not very clear. The readout of this assay could be recorded by camera whereas it includes several steps such as RNA extraction, amplification, transcription-translation coupled assay and reporter reaction. The limitations of the existing methods (RT-PCR, paper strip) and the advantages of this assay haven't been demonstrated by the experiments. The stability of RNA may also restrict the application of the proposed assay on site.
Major comments:
Authors are suggested to design an experiment to show the advantage of this assay compared with the existing method.
What is the limit of detection of this assay using LacZ and Luciferase reporter respectively?
Authors have not examined the selectivity of this assay. What is the specificity, selectivity for each of these variants? Do altering target RNA change the specificity?
In Figure 2C-F, sensor 17 showed higher fold change and sensitivity. Why was sensor 12 selected for further study in Figure 3?
Authors should show the error bar in all plots. Authors should also indicate what the error bar means (SD, S.E.M. etc.) throughout the manuscript.
Minor comments:
"This method is relatively faster but may generate false positives due to non-specific amplification and primer interactions." "using the softwares Primer 3 and NUPACK." Reference is needed.
Reference 15 belongs to CRISPR-CAS based assay but it was cited under RT-LAMP assay.
Significance
This paper will be of interest to scientists interested in developing diagnostic tools for the detection of SARS-CoV2 in viral and host pathogenic sequences; genetic disorders and development of precision medicine.
Reviewer works in the field of Chemical Biology and Nanotechnology including sensor development and the application in diagnosis, cell physiological studies.
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Reply to the reviewers
Responses to reviewers’ comments
We thank the reviewers for their encouraging comments and helpful suggestions.
Reviewer #1
(Evidence, reproducibility and clarity (Required)):
Sanchez et al report several new findings about the adhesive protrusions on Plasmodium falciparum infected erythrocytes. Using super resolution microscopy and correlation analysis, they tracked associations between the knob protein KAHRP and erythrocyte membrane cytoskeleton proteins. They have expanded on and improved previous work on the unusual spiral structure of the knobs, which appears to be a spiral ribbon or blade and have shown a developmental pathway for the association of KAHRP with the cytoskeleton. They have localised KAHRP close to the spiral and determined its abundance in the knobs. They have also used cryo electron tomography and subtomogram averaging to get an improved 3D view of the knob structure.
The work appears to be carefully and thoroughly done, and the paper is clearly written, though non specialists in the optical methods may find it challenging to navigate through the many super resolution images and correlation plots.
Comment 1: The writing needs minor editing to fix a variety of small linguistic errors and typos. For example, line 97 "sideway positions" (they presumably mean lateral location), line 980 typo overlay, line 366 "then could reorganizes", line 435, "a predict volume".
We apologize for the linguistic errors and typos. These have been corrected in the revised manuscript.
(Significance (Required)):
Comment 2: The study provides a distinct advance on the previous state of knowledge of the structure and biochemistry of the knobs. The knobs play a key role in virulence of P. falciparum and they are quite poorly understood. Although this paper does not represent a major breakthrough in determining the molecular structure or mechanistic role of the knobs, e.g. the biochemical identity of the spiral remains unknown, the new information is valuable and likely to be important in understanding the pathogenic actions of P falciparum.
We thank the reviewer for appreciating the importance of our study. We believe that our first-time observations on the dynamics of KAHRP are a very important advance in the field and that revealing the mechanistic basis is a great challenge that at the current stage has to be left to future work.
Comment 3: The interpretation shown in Figure 7 seems fine, except for the proposal that the actin cytoskeleton is reorganised. There is no evidence for that. The cryo tomograms of the cytoskeleton in Watermeyer et al addressed this point and did not find any evidence for reorganisation of the cytoskeleton other than the insertion of the knobs.
In two previous studies we could show that actin is indeed reorganized by the parasite. It is mined from the protofilaments to generate long actin filaments that connect the knobs with the Maurer’s clefts and which are used for trafficking of cargo vesicles from the Maurer’s clefts to the erythrocyte plasma membrane (Cyklaff et al. Hemoglobins S and C interfere with actin remodeling in Plasmodium falciparum-infected erythrocytes. Science. 2011 334:1283-1286; Cyrklaff et al. Oxidative insult can induce malaria-protective trait of sickle and fetal erythrocytes. Nat Commun. 2016 7:13401). Moreover, a life-cycle resolved AFM-study of the cytoplasmic side of iRBCs by the group of CT Lim has demonstrated dramatic coarsening of the spectrin network, which must be accompanied by changes to the actin component of the skeleton (Shi, Hui, et al. "Life cycle-dependent cytoskeletal modifications in Plasmodium falciparum infected erythrocytes." PLoS One 8.4 (2013): e61170). Coarsening of the actin-spectrin network would imply a decrease of the amount of actin in the network, which is consistent with its use in the parasite-derived long actin filaments.
\*Referee Cross-commenting***
I also agree with the other 2.
Reviewer #2
(Evidence, reproducibility and clarity (Required)):
Malaria parasites replicate within circulating red blood cells (RBC). During parasite maturation, the parasite coordinates extensive modification of the host cell, including structural modifications of the RBC cytoskeleton and surface membrane. These host cell alterations play crucial roles in the pathology of malaria, including vascular adhesion by parasitised cells and avoidance of splenic clearance, and so are of great interest. This interesting manuscript describes a detailed examination of the role in these RBC modifications of a well-described parasite protein called KAHRP. Using a combination of cutting-edge super-resolution microscopy, cryo-electron tomography, immuno-EM, SEM and parasite mutagenesis, the authors provide evidence that KHARP localisation alters during parasite maturation but eventually becomes closely associated with the previously-described spiral structures that underlie infected RBC surface membrane protrusions called knobs. The authors provide improved resolution of the spiral formations, generate a quantitative estimate of the number of KAHRP molecules per knob, and provide a model for the role of KAHRP in attaching other proteins to the spirals based on their observations.
In general, this study is thorough and well-performed, and the conclusions drawn are well-supported by the data. Although the work does not advance understanding of knob function or the parasite components that form the bulk of the spirals, it provides an interesting and useful contribution to understanding of the manner in which this important pathogen manipulates its host cell.
We thank the reviewer for appreciating the importance of our study and in acknowledging that it is an important intermediate step towards a complete understanding of skeleton remodelling by the parasite.
I have just a few minor suggestions that should improve the manuscript.
Comment 1: Line 91 (Page 2 paragraph 2). It would be greatly helpful here if the authors could provide a more detailed background on the makeup of the RBC cytoskeleton, and in particular the interactions between beta-spectrin and the actin protofilaments of the junctional complexes. The authors should make it clear that the actin-binding domain of beta-spectrin comprises 2 calponin like domains, and that these are attached to the end of the tandem spectrin repeat domains that make up the bulk of the molecule.
We thank the reviewer for this helpful suggestion and have added a new paragraph to the results section providing detailed background information on the makeup of the RBC membrane skeleton. The new text reads as follows:
“Major components of the red blood cell membrane skeleton are spectrin and actin filaments (Fig. 1B). The spectrin filaments consist of α- and ß-spectrin, which form α2ß2 heterotetramers by head-to-head association of two αß dimers (Lux, 2016; Machnicka et al., 2014). The N-termini of the ß-spectrin subunits are positioned at the tail ends of the heterotetramer and contain two calponin homology (CH) domains for binding to actin protofilaments consisting of 6 to 8 actin monomers in each of the two strands (Lux, 2016; Machnicka et al., 2014). Protein 4.1R strengthens the spectrin actin interaction (Lux, 2016; Machnicka et al., 2014). Groups of up to six spectrin heterotetramers can attach to an actin protofilaments, resulting in a pseudohexagonal meshwork (Lux, 2016). Ankyrin binds to the C-terminal domain of ß-spectrin and connects integral membrane proteins with the actin spectrin network in an ankyrin complex (Lux, 2016; Machnicka et al., 2014).”
Comment 2: Line 97 "These values are slightly larger than the reported physical dimension of the protofilament...". Please provide these reported dimensions here, as well as relevant references.
The requested information is now provided. The sentence now reads as follows:
“These values are slightly larger than the reported physical dimension of the protofilaments of ~37 nm (Lux, 2016) and might be explained by the lateral localization of the spectrin binding sites and the additional sizes of the primary and secondary antibody trees used to detect the two targets.”
Comment 3: Line 366 "reorganize"
The spelling mistake has been corrected.
(Significance (Required)):
Comment 4: This is a useful technical advance in understanding of the structure of the P. falciparum-infected red blood cell, and builds on the work of Watermeyer et al. (2016). The study should certainly be of interest to most malaria researchers, particularly those interested in the pathobiology of the organism.
We thank the reviewer for supporting our study.
\*Referee Cross-commenting***
I fully agree with and endorse the comments of the other 2 reviewers.
Reviewer #3
(Evidence, reproducibility and clarity (Required)):
The binding of P. falciparum infected erythrocyte (iRBCs) to the endothelium is mediated by protuberances (knobs). These knobs are assembled by a multi-protein complex at the iRBC surface. It acts as a scaffold for the presentation of the major virulence antigen, P. falciparum Erythrocyte Membrane Protein-1 (PfEMP1). The knob-associated histidine-rich protein (KAHRP) is an essential component of the knobs and therefore essential for the binding of iRBC to the endothelium under physiological conditions. This manuscript focusses on the knob architecture and KAHRP localization.
Comment 1: It is, at least for this reviewer - hard to assess how the "preparation of exposed membranes by hypotonic shock" and the analysis of the "inverted erythrocyte membrane ghosts" is i) reflective of the physiological architecture within the iRBC and ii) how the authors exclude remnants from Maurers clefts (MCs) in their preparation. The latter appears especially important for the interpretation of dynamic KAHRP repositioning, as MCs are mobile in early stages and non-mobile later on (e.g. McMilian et al. 2013, Grüring et al. 2011) and the authors observed at least some MAHRP1 signal (Figure S8), which is hard to interpret by the single representative image provided.
We understand the reviewer’s concerns, but are convinced that we have done the necessary controls to evaluate our approaches. For example, we evaluated the exposed membrane approach by investigating uninfected erythrocytes and comparing the findings with literature reports (see Figure 1). A high degree of agreement was observed. We further would like to point out that the exposed membrane approach has been successfully used by several other studies referenced in the manuscript (Dearnley et al., 2016; Looker et al., 2019; Shi et al., 2013). Please also allow us to explain why we have used exposed membranes instead of whole cells. The reason is that the hemozoin produced by the parasite interferes with STED microscopy, resulting in a quick and strong build-up of resonance energy in the specimen and, eventually, in the disruption of the cell.
With regard to the question of whether remnants of Maurer’s clefts are present in our preparations, we do not think so, at least we never observed membrane profiles reminiscent of Maurer’s clefts in SEM images of exposed membranes (see figure at the end of the response letter). Irrespectively, we will double check this result using STED imaging of exposed membranes treated with an antibody against the established Maurer’s clefts marker SBP1. These data could be added to a revised manuscript.
Comment 2: line 173: Please provide a detailed description about parasite synchronization (also absent in the methods section).
A detailed description including references are now added to the methods section:
“For synchronization of cultures, schizont-infected erythrocytes were sterile purified using a strong magnet (VarioMACS, Miltenyi Biotec) (Staalsoe et al., 1999) and mixed with fresh erythrocytes to high parasitaemia. 5000 heparin units (Heparin-sodium 25000, Ratiopharm) were added and the cells were returned to culture for 4 hrs (Boyle et al., 2010). Following the treatment with heparin, cells were washed with pre-warmed supplemented RMPI 1640 medium and then returned to culture for 2 hrs to allow for re-invasion of erythrocytes. Subsequently, cells were treated with 5% sorbitol to remove late parasite stages (Lambros and Vanderberg, 1979).”
Comment 3: line 136: Please re-check nomenclature of "PHIS1605w" (mixed nomenclature used throughout the manuscript). I suggest to use either LyMP or the up-to-date ID PF3D7_0532400.
We apologize for the oversight and now consistently use the ID PF3D7_0532400.
Comment 4: Please provide source and references for PfEMP1, MAHRP1 and "PHIS1605w" antibodies that are used. I cannot find them in the methods section or in Table S1.
We apologize for the oversight and now provide the requested information in the amended Table S1.
Comment 5: line 165: Warncke et al. (2016) appears to be misplaced as an appropriate MAHRP1 reference.
We now cite the original MAHRP1 publication by Spycher et al. 2003.
Comment 6: line 159: the sentence "The strong cross-correlation between KAHRP and actin is consistent with previous cryo-electron tomographic analysis showing long actin filaments connecting the knobs with Maurer's clefts in trophozoites (Cyrklaff et al., 2012; Cyrklaff et al., 2011; Cyrklaff et al., 2016)" could be moved to the discussion section.
The sentence was indeed redundant with a section in the discussion and was removed.
Comment 7: line 199: The text refers to Fig. 9AB - but should refer to 4AB or suppl. 11.
We are sorry for this mistake and now refer to the correct figures in the revised manuscript.
Comment 8: Fig. 4: A solid average for the number of subtomograms, but please provide information about what the arrowheads (4E) indicate.
Thank you for this comment. The arrowheads indicate peripheral crown-like densities. We have updated the figure legend to clarify this issue.
Comment 9: The "flexible periphery" is likely a combination of flexibility and occupancy as the average was made from subtomograms with varying number of turns in the spiral. As occupancy is likely a significant contributing factor to the average that should be discussed or at least mentioned.
Thank you for this important comment. Indeed, a significant variation was observed between the individual knobs. The spirals have variable diameter, and the number of peripheral proteins also varied. We added measurements to the supplementary figure 11D. In addition, we update the text and extended the discussion.
Comment 10. On that note, did the authors try and classify based on number of turns prior to averaging and if so did the authors see any differences in structures between few turn and many turn spirals?
We attempted several classifications on the full knobs with variable masks. However due to a limited number of particles in the dataset we could not converge to stable solutions. Instead, we decided to adopt the subboxing strategy where locally ordered segments at the periphery could be analyzed. This showed several structural snapshot at the periphery of the knobs.
Comment 11. What size mask was used? Was it a soft sphere around the core or big enough for the knobs with multiple spiral turns?
While we attempted several alignments and classifications with variable masks, the final refinement and measurement of FSC was performed with a soft contour mask mask. We overlaid it with the structure in Figure S11F and uploaded it as a part of the EMDB deposition. We further show the masks used in this study in a new Figure S14.
Comment 12. It might be useful for readers who are not familiar with Dynamo to provide a little bit more information about how the initial reference was produced. Additionally more information about the sub-boxing strategy ie: spacing etc. would helpful.
Thank you very much for the suggestion. For the initial reference we manually aligned all the particles, summed them up and low-pass filtered them. We now describe it in the methods section.
For the subboxing procedure we added more description to the main text:
“40 segments were extracted at the radius of the 2nd and 3rd spirals followed by their classification into structural classes.”
We further extended and simplified the description in the results section (line ~221).
Comment 13: Fig. 5 Additional (earlier) maturation stages of the iRBC with Ni2+NAT-gold-labelling would be a nice add on - this could help confirm the model and would itself be a control for the later stage labelling.
We thank the reviewer for this insightful suggestion. We are currently performing the proposed experiment and will include it in a revised version of the manuscript.
Comment 14: line 637: DMSI typo and please provide the supplier for DMSI (DSM1).
We corrected the typographic error and now provide the name of the supplier.
Comment 15: Figure 7: Please provide what the purple arrows indicate.
The figure legend has been updated.
Comment 16: Fig S11D: The labels X, Y and Z are confusing, describing the slicing axis as "XZ, YZ and XY" view is more intuitive.
Done as suggested by the reviewer.
Comment 17: Figure S13 B: WBs are cropped. Please provide un-cropped WB.
Uncropped Western blots will be provided in the revised manuscript.
(Significance (Required)):
In general, I highly appreciated the solid data and its thorough analysis of the microscopy data. The authors investigate the structural organization of knobs in iRBCs using high-resolution imaging techniques including STED and PALM super-resolution microscopy-based approaches and electron tomography. The beauty of this paper is that it does nicely re-investigate knob architecture in iRBC (e.g. Watermeyer et al., 2016, Cutts et al., 2017, Looker et al., 2019, McHugh et al., 2020) and provides some intriguing KHARP co-localization with cytoskeleton components. The downside of it is that - by nature - it is descriptive (and the data rather confirmative) and as it stands does not provide us with a deeper molecular dissection of the knob associated structure and its cellular function.
We thank the reviewer for appreciating our study and would like to emphasize the following novelties in our study:
- We show that the association of KAHRP with membrane skeletal components is highly dynamic and changes as the parasite matures. Our results on the dynamics of KAHRP organization reconciles conflicting reports in the literature, and establish for the first time a dynamical model for KAHRP organization.
- We further show that KAHRP finally assembles at remnant actin-junctional complexes devoid of the actin-capping factors adducin and tropomodulin.
- We further quantified the number of KAHRP molecules per knob and show that KAHRP is present as 60 copies per knob, a number one order of magnitude greater than previously thought.
- Last but not least, we provide a 35 Å map of the spiral scaffold underlaying knobs and show that KAHRP associates with the spiral scaffold.
We conclude by providing a novel model on the biological function of KAHRP by proposing that KAHRP acts as a glue that connects spectrin and parasite-remodeled actin filaments with the knob spiral.
\*Referee Cross-commenting***
Fully agreed.
Boyle, M.J., Wilson, D.W., Richards, J.S., Riglar, D.T., Tetteh, K.K., Conway, D.J., Ralph, S.A., Baum, J., and Beeson, J.G. (2010). Isolation of viable Plasmodium falciparum merozoites to define erythrocyte invasion events and advance vaccine and drug development. Proc Natl Acad Sci U S A 107, 14378-14383.
Lambros, C., and Vanderberg, J.P. (1979). Synchronization of Plasmodium falciparum erythrocytic stages in culture. J Parasitol 65, 418-420.
Lux, S.E.t. (2016). Anatomy of the red cell membrane skeleton: unanswered questions. Blood 127, 187-199.
Staalsoe, T., Giha, H.A., Dodoo, D., Theander, T.G., and Hviid, L. (1999). Detection of antibodies to variant antigens on Plasmodium falciparum-infected erythrocytes by flow cytometry. Cytometry 35, 329-336.
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Referee #3
Evidence, reproducibility and clarity
Summary:
The binding of P. falciparum infected erythrocyte (iRBCs) to the endothelium is mediated by protuberances (knobs). These knobs are assembled by a multi-protein complex at the iRBC surface. It acts as a scaffold for the presentation of the major virulence antigen, P. falciparum Erythrocyte Membrane Protein-1 (PfEMP1). The knob-associated histidine-rich protein (KAHRP) is an essential component of the knobs and therefore essential for the binding of iRBC to the endothelium under physiological conditions. This manuscript focusses on the knob architecture and KAHRP localization.
General point:
It is, at least for this reviewer - hard to assess how the "preparation of exposed membranes by hypotonic shock" and the analysis of the "inverted erythrocyte membrane ghosts" is i) reflective of the physiological architecture within the iRBC and ii) how the authors exclude remnants from Maurers clefts (MCs) in their preparation. The latter appears especially important for the interpretation of dynamic KAHRP repositioning, as MCs are mobile in early stages and non-mobile later on (e.g. McMilian et al. 2013, Grüring et al. 2011) and the authors observed at least some MAHRP1 signal (Figure S8), which is hard to interpret by the single representative image provided.
Specific points:
- line 173: Please provide a detailed description about parasite synchronization (also absent in the methods section)
- line 136: Please re-check nomenclature of "PHIS1605w" (mixed nomenclature used throughout the manuscript). I suggest to use either LyMP or the up-to-date ID PF3D7_0532400.
- Please provide source and references for PfEMP1, MAHRP1 and "PHIS1605w" antibodies that are used. I cannot find them in the methods section or in Table S1 -line 165: Warncke et al. (2016) appears to be misplaced as an appropriate MAHRP1 reference.
- line 159: the sentence "The strong cross-correlation between KAHRP and actin is consistent with previous cryo-electron tomographic analysis showing long actin filaments connecting the knobs with Maurer's clefts in trophozoites (Cyrklaff et al., 2012; Cyrklaff et al., 2011; Cyrklaff et al., 2016)" could be moved to the discussion section
- line 199: The text refers to Fig. 9AB - but should refer to 4AB or suppl. 11.
- Fig. 4: A solid average for the number of subtomograms, but please provide information about what the arrowheads (4E) indicate. A few additional comments on this section:
1: The "flexible periphery" is likely a combination of flexibility and occupancy as the average was made from subtomograms with varying number of turns in the spiral. As occupancy is likely a significant contributing factor to the average that should be discussed or at least mentioned.
- On that note, did the authors try and classify based on number of turns prior to averaging and if so did the authors see any differences in structures between few turn and many turn spirals?
- What size mask was used? Was it a soft sphere around the core or big enough for the knobs with multiple spiral turns?
- It might be useful for readers who are not familiar with Dynamo to provide a little bit more information about how the initial reference was produced. Additionally more information about the sub-boxing strategy ie: spacing etc. would helpful.
- Fig. 5 Additional (earlier) maturation stages of the iRBC with Ni2+NAT-gold-labelling would be a nice add on - this could help confirm the model and would itself be a control for the later stage labelling.
- line 637: DMSI typo and please provide the supplier for DMSI (DSM1).
- Figure 7: Please provide what the purple arrows indicate.
- Fig S11D: The labels X, Y and Z are confusing, describing the slicing axis as "XZ, YZ and XY" view is more intuitive.
- Figure S13 B: WBs are cropped. Please provide un-cropped WB.
Significance
In general, I highly appreciated the solid data and its thorough analysis of the microscopy data. The authors investigate the structural organization of knobs in iRBCs using high-resolution imaging techniques including STED and PALM super-resolution microscopy-based approaches and electron tomography. The beauty of this paper is that it does nicely re-investigate knob architecture in iRBC (e.g. Watermeyer et al., 2016, Cutts et al., 2017, Looker et al., 2019, McHugh et al., 2020) and provides some intriguing KHARP co-localization with cytoskeleton components. The downside of it is that - by nature - it is descriptive (and the data rather confirmative) and as it stands does not provide us with a deeper molecular dissection of the knob associated structure and its cellular function.
Referee Cross-commenting
Fully agreed.
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Referee #2
Evidence, reproducibility and clarity
Malaria parasites replicate within circulating red blood cells (RBC). During parasite maturation, the parasite coordinates extensive modification of the host cell, including structural modifications of the RBC cytoskeleton and surface membrane. These host cell alterations play crucial roles in the pathology of malaria, including vascular adhesion by parasitised cells and avoidance of splenic clearance, and so are of great interest. This interesting manuscript describes a detailed examination of the role in these RBC modifications of a well-described parasite protein called KAHRP. Using a combination of cutting-edge super-resolution microscopy, cryo-electron tomography, immuno-EM, SEM and parasite mutagenesis, the authors provide evidence that KHARP localisation alters during parasite maturation but eventually becomes closely associated with the previously-described spiral structures that underlie infected RBC surface membrane protrusions called knobs. The authors provide improved resolution of the spiral formations, generate a quantitative estimate of the number of KAHRP molecules per knob, and provide a model for the role of KAHRP in attaching other proteins to the spirals based on their observations. In general, this study is thorough and well-performed, and the conclusions drawn are well-supported by the data. Although the work does not advance understanding of knob function or the parasite components that form the bulk of the spirals, it provides an interesting and useful contribution to understanding of the manner in which this important pathogen manipulates its host cell.
I have just a few minor suggestions that should improve the manuscript.
Line 91 (Page 2 paragraph 2). It would be greatly helpful here if the authors could provide a more detailed background on the makeup of the RBC cytoskeleton, and in particular the interactions between beta-spectrin and the actin protofilaments of the junctional complexes. The authors should make it clear that the actin-binding domain of beta-spectrin comprises 2 calponin like domains, and that these are attached to the end of the tandem spectrin repeat domains that make up the bulk of the molecule.
Line 97 "These values are slightly larger than the reported physical dimension of the protofilament...". Please provide these reported dimensions here, as well as relevant references.
Line 366 "reorganize"
Significance
This is a useful technical advance in understanding of the structure of the P. falciparum-infected red blood cell, and builds on the work of Watermeyer et al. (2016). The study should certainly be of interest to most malaria researchers, particularly those interested in the pathobiology of the organism.
Referee Cross-commenting
I fully agree with and endorse the comments of the other 2 reviewers.
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Referee #1
Evidence, reproducibility and clarity
Sanchez et al report several new findings about the adhesive protrusions on Plasmodium falciparum infected erythrocytes. Using super resolution microscopy and correlation analysis, they tracked associations between the knob protein KAHRP and erythrocyte membrane cytoskeleton proteins. They have expanded on and improved previous work on the unusual spiral structure of the knobs, which appears to be a spiral ribbon or blade) and have shown a developmental pathway for the association of KAHRP with the cytoskeleton. They have localised KAHRP close to the spiral and determined its abundance in the knobs.
They have also used cryo electron tomography and subtomogram averaging to get an improved 3D view of the knob structure.
The work appears to be carefully and thoroughly done, and the paper is clearly written, though non specialists in the optical methods may find it challenging to navigate through the many super resolution images and correlation plots. The writing needs minor editing to fix a variety of small linguistic errors and typos. For example, line 97 "sideway positions" (they presumably mean lateral location), line 980 typo overlay, line 366 "then could reorganizes", line 435, "a predict volume".
Significance
The study provides a distinct advance on the previous state of knowledge of the structure and biochemistry of the knobs. The knobs play a key role in virulence of P. falciparum and they are quite poorly understood. Although this paper does not represent a major breakthrough in determining the molecular structure or mechanistic role of the knobs, e.g. the biochemical identity of the spiral remains unknown, the new information is valuable and likely to be important in understanding the pathogenic actions of P falciparum.
The interpretation shown in Figure 7 seems fine, except for the proposal that the actin cytoskeleton is reorganised. There is no evidence for that. The cryo tomograms of the cytoskeleton in Watermeyer et al addressed this point and did not find any evidence for reorganisation of the cytoskeleton other than the insertion of the knobs.
I am generally familiar with the area of this work, but not expert in the details of the optical methods and localisation analysis.
Referee Cross-commenting
I also agree with the other 2.
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Reply to the reviewers
Dear Editor,
We appreciate the critical and constructive comments that Reviewers made on our paper entitled “The structure and flexibility analysis of the Arabidopsis Synaptotagmin 1 reveal the basis of its regulation at membrane contact sites” by Benavente et al.. We are very pleased that three reviewers from Review commons appreciated the work, found it interesting and suggested constructive modifications to the paper. We have now responded to their suggestions and enclose a modified manuscript.
As suggested by the reviewers we now provide additional biochemical evidence about the role of calcium on C2 activation, more controls in the biochemical assays, an improved protocol for the lipid binding assays as well as details in the molecular dynamics. In addition, following reviewers’ recommendations, we have rephrased some of the headings and statements in the discussion section, to adjust them better to our experimental results. Altogether, we believe that the manuscript is more solid and interesting than the previous version for the general readers of eLife.
Specifically, we have made the following changes in response to the particular comments of the referees:
Reviewer 1
Major points
The conclusion that SYT1C2A determines protein behavior by binding calcium and likely switching its function from a pure tether to a lipid transporter is accurately and convincingly portrayed. However, there are some problematic statements in the way this information is interpreted and used to propose a model.
- p7: "This means that site I will be occupied depending on the physiological Ca2+ concentration to activate the protein and trigger Ca2+-dependent SYT1C2A lipid binding." Please exchange "means" by "suggests"* We agree with the reviewer and we have exchanged “means” by “suggests”
- There is not enough data to determine whether SYT1C2A interacts with the SYT1SMP domain, much less to propose that it is the SYTC2A that loads the SMP with DAG. They may also operate independently by means of the unstructured hinge sequence between them. *
- It is implied that SYTC2A would have to release its calcium atom for it to leave the PM and go to the ER to complete a single transport cycle. It is unclear whether SYT1C2A could bind and release calcium repeatedly and fast enough to cycle between membranes efficiently. It appears more plausible for it to remain at the PM until intracellular calcium concentrations decrease. **
These statements should be marked as speculative. *
We understand that the reviewer comments are related to steps 3 and 4 of our model for the function of SYT1 (figure7; pages 17 and 18). We have now included these scenarios suggested by the reviewer (page 17 and 18). In addition, we have discussed the work from Vennekate et al, PNAS, 2012, related to the cis and trans membrane interactions of the two C2 domains of human synaptotagmin (Syt1). The authors demonstrated that they are driven by the balance in the concentration of anionic lipids between target membranes and by Ca2+ and protein concentration. Likewise, the changes in the local composition of PIP and/or Ca2+ may drive the transfer of SYT1C2A from the PM to de ER and vice versa while the C2B remains at the PM.
Most of the graphs shown (except Fig. 4A) appear to show only one experiment. Please include results from at least three independent experiments in all graphs, and analyze them statistically. Please describe only differences between samples that are statistically significant (for all graphs and tables).
Following reviewed recommendation, we have assured that all the biochemical data arises from three independent measurements. Indeed, as indicated in the figure legends and methods section, this was the case for the Ca2+ binding experiments at figure 2C and for the lipid binding data at figure 4. We have now repeated the ITC experiments to provide three independent measurements of the dissociation constant of SYT1C2A for Ca2+.
Minor comments
Please include the PDB codes for the available structures used. It is not clear where the C2C domain structure comes from. We guess it may correspond to PDB entry 2DMG. A word of caution, this 2006 structure has been released but not published and its quality is suboptimal. After its appearance in Idevall-Hagren et al. 2015 supplementary images it has been re-cited in other publications. I would advise against making topology claims based on this structure (Figure S1), and only use it as an example for polybasic patches in C2 domains.
We have included the PDB codes for the available structures used at the corresponding figure captions 1, 3 and S1.
We agree that the stereochemistry of the refined structure of the E-Syt2 C2C domains (2DMG) is suboptimal. However, we have sought for the advice of an NMR expert (M.A. Jimenez, https://scholar.google.es/citations?hl=es&user=iAF0ymYAAAAJ) to evaluate the NMR restrains available alongside the entry at PDB. She concluded that the Halpha-Halpha distance restrains indicate that the connectivity of the beta strands is correct. The confusion may arise from the fact that the PDB entry has been updated twice since 2006, the last one in 2011.
- p4: Schauder et al. 2014. Only the "shuttle" model is mentioned in the text. Although this may be the most plausible scenario, the "tunnel" model cannot be completely ruled out*. We have now stated that both shuttle or tunnel modes are possible for lipid transfer at page 4.
- p5: Fernandez-Busnadiego et al. 2015 does not make a reference to the claim in the text.* Fernandez-Busnadiego et al. 2015 has been replaced by Collado et. al 2019
- p18: Collado et. al 2019 don't assign the peak-forming function to the N-terminal hairpin domain of tricalbins. As the reviewer indicates, Collado et. al 2019 just suggests that the peak forming function could be due to the N-terminal hairpin domain of tricalbins: “This phenomenon may rely on the hairpin sequence that anchors Tcbs to the ER membrane. Tcb hairpin sequences could sense and/or generate membrane curvature as in reticulons and other ER morphogenetic proteins (Hu et al., 2011).” (Taken from Collado et al. 2019).*
Accordingly, we have indicated that “It has been suggested that the insertion of the N-terminal hydrophobic end of Tcbs may induce the formation of peaks of strong curvature at the ER region facing the PM. These structures shorten the distance between the ER and the PM by ~7 nm and facilitate lipid transport (Collado et al., 2019)”
Fig. 1A: the notation for the domains C2C-C2E of E-Syt1 is confusing and not described in the legend. Also, please mark which beta sheet is which more clearly in Fig 1B, it is very difficult to understand the labelling** Fig. 1C: several elements (e.g. types of boxes, "T" on the top) used in the figure are not described in the legend. Both beta sheets and mutations are described as "arrows" in the legend, please differentiate between vertical and horizontal.
We have modified the Fig. 1A legend to explain the notation of C2 domains of human E-Syts “Human E-Syt1 displays five C2 domains while E-Syt2 and E-Syt3 display three”.
Labeling of beta strands has been modified to make the panel clearer.
We have rewritten the caption of figure 1C to describe the types of boxes and the “T” and to distinguish between vertical and horizontal arrows.
Fig. 2A: indicate Lys 286, which is mentioned in the text
The reference to Lys 286 in the text was not correct. We have modified the text to indicate that Lys275 replaces the Ca I as it is shown in figure 2.
Fig. 2B: Inset too small to read.
Labels for inset at Fig 2B have been enlarged.
Fig. 3: please show the scale and explain the blue-red color code. Please mark the polybasic patch.
We have explained the meaning of the blue and red code, marked the polybasic patch of SYT1C2A and E-Syt1C2C and indicated that all of them are scaled to the same value.
Fig. 4A should show both mutants for both types of liposomes.
We have included new liposome binding data including both mutants for both types of liposomes.
Table 1: what is "control"?
We have indicated that the unbound wild-type protein is taken as a control
Fig. S5: Difficult to read, increase font size. The text talks about experiments with calcium and EGTA that are not shown in the figure.
We have increased figure size to facilitate reading. We have also indicated that C2AB-Ca and C2A stand for the experiments carried out in presence of Ca and EGTA, respectively.
Reviewer 2
Minor comments
Typos: please re-read carefully through the manuscript to remove them. We advise the authors to have the manuscript corrected by a native english-speaker.
We have done a thorough revision of the manuscript to correct typos and to improve the English style of the manuscript
Reviewer 2 considers that “The authors discuss their findings within the frame of experimental observations that are already published but these remain speculative”
We are glad that the reviewer appreciates our work in “decrypting the roles of C2 individual operating modes” as it is a “central issue for providing functional specificity but also plasticity in response to developmental /environmental clues”. The reviewer also considers our work “important and identifies a number of very interesting features”. As already mentioned to the editor, the present version of the manuscript includes new biochemical data and analysis to support further the functions of C2A-C2B tandem. In addition, we have included new references and rephrased some of the headings and statements in the discussion section, to adjust them better to our experimental results.
Reviewer 3
Major points
1)The authors investigated SYT1C2A calcium-binding sites using two different methods, ITC and differential scanning fluorimetry. By using ITC, they described the first binding site coordinating calcium ions in the nanomolar range. The second calcium-binding site was then characterized by differential scanning fluorimetry. The second calcium-binding site binds calcium with Kd of 277 µM. The authors then mutated SYT1C2A at two positions and performed again differential scanning fluorimetry. In this case, they did not observe any blue shift in intrinsic fluorescence concluding that "calcium-binding is mediated by the calcium-binding site". It is not clear which binding site the authors mean. In the structure of SYT1C2A, the mutated residues (D276 and D282) are shared by both calcium-binding sites. It is, therefore, difficult to interpret the data. The authors should generate a unique mutation for each site and perform both ITC and differential scanning fluorimetry
The SYT1C2A-DADA double mutant was prepared to abolish Ca2+ binding to both site I and site II and to discard an unspecific effect of Ca2+ on intrinsic fluorescence that accounts for the low affinity Kd. Our data showed that the addition of Ca2+ to SYT1C2A-DADA does not produce a shift in intrinsic fluorescence of the protein; indicating that the observed Ca2+-binding activity is specifically mediated by the Ca2+ dependent lipid binding site. We clarify this point in the present version of the manuscript.
In addition, following reviewer’s recommendation, we have prepared two additional point mutant proteins, SYT1C2A D276A and SYT1C2A E340A, to investigate the Ca2+ binding properties at site II and I, respectively. As expected, the reduction of one carboxylate ligand at the structural site II produces a drastic decrease in the Ca2+ binding affinity (Kd = 1.8± 0.5 mM) which is coupled with a decrease in thermal stability of the protein (Ti = 55°C) and a red-shift in fluorescence emission with respect to the wild type protein that resembles those effects observed for the SYT1C2A-DADA mutant (Figure S2A). Differentially, SYT1C2A Glu334Ala doubled the Kd (534 ± 60 mM) while reducing slightly its thermal stability (page 7 figure S2A)
2)The authors described an increase in the inflexion point temperature with increasing calcium concentration. They noted that the effect was measurable from 30 µM to 300 µM. Looking at the plot with the first derivative ratio (Figure 2C), there is also an apparent change in the inflexion point temperature from 300 µM to 3 mM. Does this mean that the SYT1C2A domain binds more than two calcium ions?
The ligand induced stabilization of proteins results in changes of the thermally induced melting curves for the ligand complexed relative to the uncomplexed proteins. This effect is used to unequivocally identify ligand hits for a particular protein from large libraries of compounds and to provide an initial estimation of the binding affinity. However, a deeper analysis of the ligand binding affinities using this technique is discouraged as the increase of melting temperature with the ligand concentration does not saturate to a particular value. This is why the effect of Ca2+ addition to SYT1C2A was also measurable from 300 µM to 3 mM, and it does not necessarily imply the binding of Ca2+ to another site. Consequently, we used other techniques such as ITC or the analysis of the change of intrinsic fluorescence upon Ca2+ addition to precisely characterize the Ca2+ binding affinities of SYT1C2A. In the present version of the manuscript, we have indicated that the change in Ti vs Ca2+ concentration is measurable when moving from 30 mM to 300 mM, thus demonstrating a Ca2+-binding event “is initiated” in this concentration range (page 7)
3)To address lipid-binding properties of the SYT1 C2 domains, the authors used two independent methods, lipid co-sedimentation assay and BLI. In the Material and Methods section, the authors wrote that a solution of liposomes was sonicated for seven minutes to achieve homogeneity. How was homogeneity checked? Standard protocols for the liposome co-sedimentation assay use the extruder to achieve a homogeneous population of the liposomes. Also, the authors noted that the liposomes were resuspended in the buffer containing 50 mM Tris/HCl, 80 mM KCl, and 5 mM NaCl. The liposomes are usually loaded with sugar molecules, like raffinose at this step to allow subsequent co-sedimentation using centrifugation.
Following the reviewer recommendation, we have used an extruder to achieve a homogeneous population of the liposomes (see the Methods section). This has produced an improvement of the data from the statistical point of view. However, we did not employ any sugar to facilitate lipid sedimentation as we found that 1 hour centrifugation at 58,000 rpm using a TLA100 rotor (Beckman) was enough to separate adequately soluble and precipitated fractions.
The authors wrote that the samples were centrifuged at 58,000 rpm. The information does not allow reproducibility without rotor specification.
We have now included the rotor specification in the methods section.
The bound protein was estimated by subtracting the supernatant from the total amount of protein used in the assay. Direct estimation of the protein amounts in the bound fraction via e.g. SDS-PAGE would be more suitable.
We respectfully disagree with the reviewer in this issue. The reviewer may note that the differences in the fraction of bound protein to the liposomes are at maximum around 25%. Such values are statistically significant using spectrophotometric techniques but there will be less accurately determined by the analysis of an SDS-PAGE. In addition, the later would require several washing steps of the insoluble fraction that may induce additional errors. This is well documented in a previous work from our group (Diaz et al, PNAS 2015). There, the lipid binding properties of WT and mutant C2 domain are compared using both approaches; in this work it is shown that the spectrophotometric techniques showed significant differences with the SDS-PAGE, which resulted just indicative.
Nevertheless, we have prepared the requested SDS-PAGE for reviewer evaluation (see below) and if required we will include it as a new panel in figure 4 or include it as supplementary material. The SDS-PAGE shows the amount of soluble protein after the incubation with liposomes. It is clearly shown a reduction in the amount of WT and DADA soluble protein upon incubation with PCPSPI liposomes with respect to the sample incubated with PCPS liposomes. Differentially, no effect is observed for the PolyB and WT in presence of EGTA. Sample migrates abnormally producing a double band in presence of EGTA, probably due to the effect of removing the structural Ca site.
Critical controls for the liposome co-sedimentation assay are missing:
Do the SYT1 C2 domains bind liposomes without negatively charged lipids (i.e. PC-only liposomes)?
Does the SYT1C2A-DADA mutant domain bind the PC/PS/PI liposomes?
Does the SYT1C2A-PolyB mutant interact with the PC/PS liposomes?
We have included all the controls suggested by the referee in the present version of the manuscript, in the results section and in figure 4A.
The authors wrote both in the main text and the figure 4 legend that they used a lipid monolayer in the BLI method. However, in the Material and Methods section, they wrote that they used small unilamellar vesicles.
The starting material for lipid monolayer immobilization at the biosensor tip is a solution of small unilamellar vesicles. We have clarified this issue in the methods section.
4)The authors beneficially used all-atom MD simulations to address mechanistic details of the SYT1 C2 domains with two different lipid bilayers. However, several issues need to be addressed.
Is there a particular reason to include sitosterol in the MD simulations? Does sitosterol contribute to protein binding?
We clarify this issue in the present version of the manuscript. The use of sitosterol or stigmasterol in research involving plant membranes and membrane-associated proteins is recommended (DOI: 10.1063/1.4983655 PMID: 28595398) to recapitulate the fluidity and thermotropic properties of model membranes (DOI: 10.1016/j.colsurfb.2019.110422 PMID: 31437609). Sitosterol, as is the case for cholesterol in mammal membranes, contributes to packing the lipid bilayer more tightly into a liquid ordered phase (DOI: 10.1016/j.chemphyslip.2017.01.003 PMID: 28088325) and this aspect is important in molecular dynamics simulations to attain equilibration more effectively (DOI: 10.1016/j.jcis.2011.02.048 PMID: 21429500).
We observed one hydrogen bond contact between Asn 338 at loop L3 and sitosterol in PSPI-M. We clarify this point in the results section.
Why was not the simulation ran for a longer time? What was a criterion to determine that the system reached a stable state? Results of the MD simulations are presented as static snapshots. The manuscript would benefit from a more detailed analysis, e.g. the number of hydrogen bonds between the protein and phospholipid molecules over time, development of the tilt angle over time, etc.
Following the reviewer’s recommendations, we now provide data showing the dynamic features of our MD calculations. In particular, we have compared the overlay of the different structures along the simulation of the SYT1C2A domain attached to the PS-Membrane and to the PSPIP-Membrane highlighting those amino acids hydrogen bonded to phospholipids (Figure S4A and S4B). This picture illustrates well that the pattern of interactions is conserved along the simulation. In addition, it also shows that the orientation of the domain with respect to the plane of the membrane is conserved. In this respect, as the reviewer requested, we have also included, a picture illustrating the change in the tilt angle of the C2A with respect to the plane of the membrane along the simulation. This analysis reveals that the tilt angle with respect to the membrane is 20 degrees larger for the PSPIP-Membrane than for the PS membrane due to the interaction of PIP molecules with the polybasic site (Figure S4E).
In addition, we now present time traces illustrating the course of the simulations. In particular, those corresponding to the RMSD of the individual SYT1C2A, SYT1C2B and the linker between them. They clearly show that the simulations reached equilibrium within the time sampled (Figure S5H).
The authors performed the MD simulations for both SYT1 C2 domains. It would be informative to include an electrostatic potential mapped on the surface of the SYT1C2B domain similarly to figure 3. The experimental results showed that SYT1C2B binds liposomes containing PC/PS. How does SYT1C2B interact with the PC/PS membrane? The authors noted that SYT1C2 inserts loop L3 into the lipid bilayer and that this loop adopts a β-hairpin structure. This is the case for the simulation with the SYT1C2AB fragment, but not for the SYT1C2B domain alone. Is the β-hairpin formed during the MD simulation? Or is it a result of the template-based modelling?
To clarify reviewers’ concerns, we have included a supplementary figure illustrating the RMSD per residue along the MD simulation for the SYT1C2AB protein fragment in solution, and attached to PSPI-M. The representation illustrates an overall reduction of the RMSD as a result of the protein stabilization at the membrane, which is more significant at the membrane binding loops. In particular, the highly flexible SYT1C2B L3 loop in solution becomes highly stabilized upon membrane interaction and it folds as a beta hairpin.
We have calculated the electrostatic potential mapped on the surface of the SYT1C2B. As it does not come from an experimental structure, we decided not to include in figure 3. The map, which is depicted below in the orientation shown in figure 3, shows that SYT1C2B might not display a polybasic site in accordance with our experimental results.
How is the proposed binding model of the SYT1C2AB affected by the data obtained using SAXS?
SAXS data showed that SYT1C2AB fragment may adopt a V-shaped compact structure and an extended conformation in which there is no interaction between the C2A and C2B domains. Interestingly, the V-shaped structure in solution resembles the proposed binding mode for SYT1C2AB to the membrane. We clarify this point in page 15.
Minor comments
1) SYT1CB construct is not listed in figure 1A along with the other constructs used in the study.
We have modified Figure 1B to include SYT1C2B
2) Phospholipids contain a phosphate group rather than a phosphoryl group.
We have modified the text to correct this.
3) In the text, the authors sometimes used the ratio 350 nm/330 nm and sometimes 330 nm/350 nm.
This has been corrected in Figure 2C
4) Figure S2, displayed curves look strikingly similar, different line representation does not allow a proper comparison. There are no units for y-axes.
The figure has been corrected according to the reviewer’s recommendation for proper comparison.
5) Figure 4B, y-axes do not have scales.
The Y-axis from the BlitZ system represents the thickening of the layer of proteins attached to the biosensor tip and it is given in nm. However, this parameter could be meaningless when comparing different membranes and/or proteins. Hence, we scaled the plots to the maximum thickness for comparison purposes.
6) Figure 5B, IP3 or I3P?
We have corrected the labels corresponding to inositol triphosphate IP3 at figure 5B
7) The authors noted that based on their SAXS experiments, the SYT1-SMPC2A has a maximum size of 176 Å and they wrote that this value is in accordance with the size of the previously characterized E-Syt2-SMPC2AB protein. However, as the authors reported, E-Syt2-SMPC2AB is two times smaller.
We agree with the reviewer, the size of the SMP tunnel of E-Syt2-SMPC2AB is two times smaller than the Dmax size of SYT1 SMPC2A. We clarify this point in the text.
Yours sincerely
Armando Albert
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Referee #3
Evidence, reproducibility and clarity
The focus of this manuscript is the structural characterization of Arabidopsis synaptotagmin 1 (SYT1), which is a plant ortholog of the mammalian extended synaptotagmins (E-Syts). E-Syts play a principal role in the non-vesicular lipid transfer at the endoplasmic reticulum - plasma membrane contact sites. The function of the extended synaptotagmins is given by a unique combination of the evolutionarily conserved domains. The authors combined both experimental and computational methods to characterize different domains of Arabidopsis SYT1.
The authors solved the structure of one of the SYT1 C2 domains (SYT1C2A) using X-ray crystallography. The obtained structure is highly similar to the previously characterized C2A domain of mammalian E-Syt2. In contrast to the orthologous C2A domain of E-Syt2, only two calcium ions are coordinated by the SYT1C2A domain. Next, the authors aimed to characterize the identified calcium-binding sites by two different experimental techniques, namely isothermal titration calorimetry (ITC) and differential scanning fluorimetry. To study lipid interactions of SYT1, the authors used a combination of the experimental approach (liposome-binding assays and biolayer interferometry, BLI) and computational methods (ligand-protein docking and molecular dynamics simulations). The authors found that both SYT1 C2 domains can interact with the lipid bilayer containing anionic phospholipids. Intriguingly, the authors described two lipid-interacting sites in the SYT1C2A domain. One site is involved in the coordination of phosphatidylserine (PS) in a calcium-dependent manner, and the second one coordinates molecules of phosphatidylinositol 4,5-bisphosphate (PIP2) through mostly electrostatic interactions. Last, the authors study the flexibility of SYT1 using partially overlapping protein fragments via small-angle X-ray scattering. Three hinge points are suggested to be responsible for the high flexibility of SYT1.
The notion that SYT1C2A domain confers two independent lipid-binding sites, one unique for PIP2 molecules, and the second one regulated by calcium ions, is very compelling. In addition, the results describing the potential SYT1 flexibility provide novel insight into the function of extended synaptotagmins. However, my enthusiasm is mitigated by several points listed below:
1)The authors investigated SYT1C2A calcium-binding sites using two different methods, ITC and differential scanning fluorimetry. By using ITC, they described the first binding site coordinating calcium ions in the nanomolar range. The second calcium-binding site was then characterized by differential scanning fluorimetry. The second calcium-binding site binds calcium with Kd of 277 µM. The authors then mutated SYT1C2A at two positions and performed again differential scanning fluorimetry. In this case, they did not observe any blue shift in intrinsic fluorescence concluding that "calcium-binding is mediated by the calcium-binding site". It is not clear which binding site the authors mean. In the structure of SYT1C2A, the mutated residues (D276 and D282) are shared by both calcium-binding sites. It is, therefore, difficult to interpret the data. The authors should generate a unique mutation for each site and perform both ITC and differential scanning fluorimetry.
2)The authors described an increase in the inflexion point temperature with increasing calcium concentration. They noted that the effect was measurable from 30 µM to 300 µM. Looking at the plot with the first derivative ratio (Figure 2C), there is also an apparent change in the inflexion point temperature from 300 µM to 3 mM. Does this mean that the SYT1C2A domain binds more than two calcium ions?
3)To address lipid-binding properties of the SYT1 C2 domains, the authors used two independent methods, lipid co-sedimentation assay and BLI. In the Material and Methods section, the authors wrote that a solution of liposomes was sonicated for seven minutes to achieve homogeneity. How was homogeneity checked? Standard protocols for the liposome co-sedimentation assay use the extruder to achieve a homogeneous population of the liposomes. Also, the authors noted that the liposomes were resuspended in the buffer containing 50 mM Tris/HCl, 80 mM KCl, and 5 mM NaCl. The liposomes are usually loaded with sugar molecules, like raffinose at this step to allow subsequent co-sedimentation using centrifugation. The authors wrote that the samples were centrifuged at 58,000 rpm. The information does not allow reproducibility without rotor specification. The bound protein was estimated by subtracting the supernatant from the total amount of protein used in the assay. Direct estimation of the protein amounts in the bound fraction via e.g. SDS-PAGE would be more suitable. Critical controls for the liposome co-sedimentation assay are missing. Do the SYT1 C2 domains bind liposomes without negatively charged lipids (i.e. PC-only liposomes)? Does the SYT1C2A-DADA mutant domain bind the PC/PS/PI liposomes? Does the SYT1C2A-PolyB mutant interact with the PC/PS liposomes? The authors wrote both in the main text and the figure 4 legend that they used a lipid monolayer in the BLI method. However, in the Material and Methods section, they wrote that they used small unilamellar vesicles.
4)The authors beneficially used all-atom MD simulations to address mechanistic details of the SYT1 C2 domains with two different lipid bilayers. However, several issues need to be addressed. Is there a particular reason to include sitosterol in the MD simulations? Does sitosterol contribute to protein binding? Why was not the simulation ran for a longer time? What was a criterion to determine that the system reached a stable state? Results of the MD simulations are presented as static snapshots. The manuscript would benefit from a more detailed analysis, e.g. the number of hydrogen bonds between the protein and phospholipid molecules over time, development of the tilt angle over time, etc. The authors performed the MD simulations for both SYT1 C2 domains. It would be informative to include an electrostatic potential mapped on the surface of the SYT1C2B domain similarly to figure 3. The experimental results showed that SYT1C2B binds liposomes containing PC/PS. How does SYT1C2B interact with the PC/PS membrane? The authors noted that SYT1C2 inserts loop L3 into the lipid bilayer and that this loop adopts a β-hairpin structure. This is the case for the simulation with the SYT1C2AB fragment, but not for the SYT1C2B domain alone. Is the β-hairpin formed during the MD simulation? Or is it a result of the template-based modelling? How is the proposed binding model of the SYT1C2AB affected by the data obtained using SAXS?
Minor comments:
1) SYT1CB construct is not listed in figure 1A along with the other constructs used in the study.
2) Phospholipids contain a phosphate group rather than a phosphoryl group.
3) In the text, the authors sometimes used the ratio 350 nm/330 nm and sometimes 330 nm/350 nm.
4) Figure S2, displayed curves look strikingly similar, different line representation does not allow a proper comparison. There are no units for y-axes.
5) Figure 4B, y-axes do not have scales.
6) Figure 5B, IP3 or I3P?
7) The authors noted that based on their SAXS experiments, the SYT1-SMPC2A has a maximum size of 176 Å and they wrote that this value is in accordance with the size of the previously characterized E-Syt2-SMPC2AB protein. However, as the authors reported, E-Syt2-SMPC2AB is two times smaller.
Significance
Nature and significance of the advance:
By a combination of experimental and computational methods, the manuscript provides novel insight into the structure-function relationship of plant SYT1.
Work in the context of the existing literature:
The submitted manuscript deals with Arabidopsis SYT1 protein, which belongs to an evolutionarily conserved family of proteins functioning at the ER-PM contact sites. Several recent reports described a principal role of Arabidopsis SYT1 in the regulation of lipid homeostasis, plasmodesmata functions and the response to various stresses (Lee et al. 2019. Ionic stress enhances ER-PM connectivity via phosphoinositide-associated SYT1 contact site expansion in Arabidopsis. PNAS 116, 1420-1429. https://doi.org/10.1073/pnas.1818099116; Ishikawa et al. 2020. Structural and functional relationships between plasmodesmata and plant endoplasmic reticulum-plasma membrane contact sites consisting of three synaptotagmins. New Phytologist 226, 798-808. https://doi.org/10.1111/nph.16391; Ruiz-Lopez et al. 2021. Synaptotagmins at the endoplasmic reticulum-plasma membrane contact sites maintain diacylglycerol homeostasis during abiotic stress. The Plant Cell. https://doi.org/10.1093/plcell/koab122). However, in contrast to mammalian orthologs, mechanistic details of the plant SYT1 function are largely missing.
Audience:
The manuscript might be of interest to the community of plant molecular biologists, structural biologists dealing with peripheral membrane proteins and computational biologists.
Reviewer's expertise:
Reviewer's field of expertise is plant molecular biology, plant biochemistry, protein-protein, protein-membrane and ion-membrane interactions, molecular dynamics simulations, integrative structural biology, structural bioinformatics.
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Referee #2
Evidence, reproducibility and clarity
This work focuses on Synaptotagmin1 (SYT1), a regulatory element of plant membrane contact site, that act as a tether and physically and functionally connects the endoplasmic reticulum (ER) to the plasma membrane (PM). Like many membrane contact site proteins, SYT1 harbours lipid transfer activity through its SMP domain. Plant SYTs proteins are orthologous to the Extended Synaptotagmin and Tricalbin ER-PM tethers from animal and yeast. SYT1 presents two C2 (C2A and C2B) lipid-binding domains at their C-terminus that are determinant for PM binding, presumably regulating SYT1 function at ER-PM membrane contact sites.
In this paper, Benavente et al. aimed at investigating the molecular mechanisms of SYT1 binding to the PM and specificity of function of C2A (previous work has shown that SYT1 C2A, but not SYT1 C2B, binds membrane lipids in a Ca2+ dependant manner). The authors combined a wide range of approaches from X-ray crystallography to biophysics and in silico molecular modelling to understand the mechanisms of SYT1 C2A interaction with lipids, at the molecular level. From their study, Benavente et al. shows that C2A display dual lipid binding activity interacting with PS in a Ca2+-dependant manner and with phosphoinositide in a Ca2+-independent manner. These interactions involve two distinct sites; a polybasic amino acid site for phosphoinositides binding and a Ca2+-dependant lipid binding site for PS. They propose that this two-steps binding mechanism confers plasticity in membrane docking under low and high intracellular calcium concentration. They also show that SYT1 full length protein displays three flexible hinges, which they propose confers SYT1 a high degree of conformational freedom
Minor comments
- Typos: please re-read carefully through the manuscript to remove them.
- We advise the authors to have the manuscript corrected by a native english-speaker.
Significance
C2- domains are central functional elements of SYT/E-SYT/Tricalbin ER-PM tethers. They regulate PM docking through their lipids binding activity, which can be calcium-dependant or calcium-independent, but also presents lipid specificity (PS, phosphoinositides...). Beside their lipid-binding activity, C2 domains have also been shown to be involved in protein-protein interaction, including intramolecular interaction to inhibit lipid-transfer activity (E-SYT). Multiple C2s are present in SYT/E-SYT/Tricalbin tethers and their diversity of function is likely central for providing functional specificity but also plasticity in response to developmental /environmental clues (together with changes membrane lipid composition and intracellular calcium levels). Decrypting C2 individual operating mode is therefore central. This work is important as it investigates SYT1A docking mechanisms at the molecular level and identifies a number of very interesting features. However, as it stands, the paper does not make the link with SYT1 functionality. The authors discuss their findings within the frame of experimental observations that are already published but these remain speculative.
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Referee #1
Evidence, reproducibility and clarity
Summary:
Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate). The authors obtain a high-resolution structure of SYT1C2A and characterize its calcium and lipid-binding capabilities and those of SYT1C2B. They also study the influence of these interactions on domain topology and the overall architecture of SYT1. They uncover a calcium-dependent lipid binding mechanism that allows them to propose an interesting model in which SYT1C2A binds to the PM to help shuttle DAG to the ER upon abiotic stress.
Major comments:
- Are the key conclusions convincing? - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? The conclusion that SYT1C2A determines protein behavior by binding calcium and likely switching its function from a pure tether to a lipid transporter is accurately and convincingly portrayed. However, there are some problematic statements in the way this information is interpreted and used to propose a model.
• p7: "This means that site I will be occupied depending on the physiological Ca2+ concentration to activate the protein and trigger Ca2+-dependent SYT1C2A lipid binding." Please exchange "means" by "suggests".
• There is not enough data to determine whether SYT1C2A interacts with the SYT1SMP domain, much less to propose that it is the SYTC2A that loads the SMP with DAG. They may also operate independently by means of the unstructured hinge sequence between them.
• It is implied that SYTC2A would have to release its calcium atom for it to leave the PM and go to the ER to complete a single transport cycle. It is unclear whether SYT1C2A could bind and release calcium repeatedly and fast enough to cycle between membranes efficiently. It appears more plausible for it to remain at the PM until intracellular calcium concentrations decrease. These statements should be marked as speculative.
- 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. No new experiments suggested.
- Are the data and the methods presented in such a way that they can be reproduced? Yes, to the best of my knowledge.
- Are the experiments adequately replicated and statistical analysis adequate? No. Most of the graphs shown (except Fig. 4A) appear to show only one experiment. Please include results from at least three independent experiments in all graphs, and analyze them statistically. Please describe only differences between samples that are statistically significant (for all graphs and tables).
Minor comments:
- Specific experimental issues that are easily addressable. No issues with experiments.
- Are prior studies referenced appropriately? Generally yes, but there are a few things to change:
• Please include the PDB codes for the available structures used. It is not clear where the C2C domain structure comes from. We guess it may correspond to PDB entry 2DMG. A word of caution, this 2006 structure has been released but not published and its quality is suboptimal. After its appearance in Idevall-Hagren et al. 2015 supplementary images it has been re-cited in other publications. I would advise against making topology claims based on this structure (Figure S1), and only use it as an example for polybasic patches in C2 domains. • p4: Schauder et al. 2014. Only the "shuttle" model is mentioned in the text. Although this may be the most plausible scenario, the "tunnel" model cannot be completely ruled out. • p5: Fernandez-Busnadiego et al. 2015 does not make a reference to the claim in the text. • p18: Collado et. al 2019 don't assign the peak-forming function to the N-terminal hairpin domain of tricalbins.
- Are the text and figures clear and accurate? Generally yes, although the figures and legends should contain more information. For example:
- Fig. 1A: the notation for the domains C2C-C2E of E-Syt1 is confusing and not described in the legend. Also, please mark which beta sheet is which more clearly in Fig 1B, it is very difficult to understand the labelling.
- Fig. 1C: several elements (e.g. types of boxes, "T" on the top) used in the figure are not described in the legend. Both beta sheets and mutations are described as "arrows" in the legend, please differentiate between vertical and horizontal.
- Fig. 2A: indicate Lys 286, which is mentioned in the text.
- Fig. 2B: Inset too small to read.
- Fig. 3: please show the scale and explain the blue-red color code. Please mark the polybasic patch.
- Fig. 4A should show both mutants for both types of liposomes.
- Table 1: what is "control"?
- Fig. S5: Difficult to read, increase font size. The text talks about experiments with calcium and EGTA that are not shown in the figure.
Text:
- p5, first Results paragraph: reference the loop numbers marked in the figure to facilitate the description. The description of the loop between b6 and b7 is not clear: the text implies it is not present in SYT1C2A, although it should say it is unstructured.
- Please indicate more prominently throughout the text and methods the plant species from which the C2 domains were studied, rather than just saying "plant". For example, are all the other SYTs shown in Fig 1C from Arabidopsis as well? To generalize the findings reported here as "plants", the conservation in other species need to be shown. Alternatively, please rephrase the relevant statements.
- "Data" is used both in singular and plural.
- There are several typos (it would be much easier to point to them having line numbers in the manuscript!), e.g. p6 title says "C2+" and the next paragraph "SYTCA2", Fig. 4D is mentioned in the text but it doesn't appear in the figures, p16: "DAG form the PM" -> from, p17 "overexpression of Syt1" -> E-Syt1.
- Do you have suggestions that would help the authors improve the presentation of their data and conclusions? References to abiotic stress leading to DAG accumulation can be found throughout the paper, but little is explained about how this correlates with the increase in calcium concentration suggested for SYT1 activation. It would be an improvement to explain how this happens.
Significance
- Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.
Multi-C2 domain proteins perform multiple different functions through mechanisms not yet fully understood. One important reason for this lack of knowledge is the presence of multiple C2 domains and their similarity to each another. The key to understanding how a C2 domain operates can hinge on a single calcium-binding site, which often escape accurate prediction by homology modelling and other computational methods. This is also the case for lipid binding affinity and stereophysical properties of any protein.
This work highlights the importance of obtaining reliable, high-resolution structures of these domains as well as characterizing their binding partners and the dynamics of their interactions. Through the identification of the properties of each C2 domain and adjacent sequences the authors provide a coherent mechanistic model for SYTC2AB and a reproducible workflow for the study of other C2 domains.
- Place the work in the context of the existing literature (provide references, where appropriate). This work is an important step in the study of plant synaptotagmins, in which previously reported SYT1 biochemical properties (Schapire 2018, Perez-Sancho 2015, among others) and the study of its orthologs in other organisms are brought together with novel structural and biophysical data to create a compelling mechanistic model. It also has important implications for the mechanisms of functions of this family of proteins in other organisms.
- State what audience might be interested in and influenced by the reported findings. Researchers in the broad membrane traffic community will enjoy this work, and particularly those working with orthologs of SYT1 might find insights that apply to their research. In a broader sense, this work will be appealing to researchers working in plant cellular stress response.
- 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. Structure of ER-PM contact sites. I have no expertise in titration calorimetry or SAXS and cannot properly evaluate those results.
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Reply to the reviewers
We are grateful to the reviewers for their thoughtful comments and propose the following experiments or clarifications listed below (blue) in a revised manuscript.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
The authors use a combination of Dsn1-Flag kinetochore purification from yeast extracts and laser trapping experiments (as in a number of previous studies), to study the effect of Mps1-dependent phosphorylation on reconstituted kinetochore-microtubule attachments in vitro. They complement this analysis with genetic experiments characterizing the effects of non-Mps1 phosphorylatable mutants on checkpoint activity and chromosome segregation in yeast.
The authors had previously shown that Mps1 is the major kinase activity that copurifies with Dsn1-Flag in their purification scheme. They now investigate the effect of adding ATP and thereby allowing Mps1 phosphorylation in the reconstituted system. They show that addition of ATP decreases the rupture force of kinetochore-microtubule attachments, meaning it weakens the strength of the attachment. This effect can be negated either by inhibiting Mps1 with reversine, or by providing kinetochores in which the Mps1 phosphorylation sites on Ndc80 (most of them in the N-terminal tail) have been mutated to alanine. Thus, like the activity of Ipl1, Mps1 phosphorylation of the Ndc80 N-tail (which is known to be important for full MT affinity) weakens kinetochore-microtubule attachments.
Cellular experiments demonstrate that non-Mps1 phosphorylatable Ndc80 14-A mutants have a functional mitotic checkpoint (contrary to previous claims by Kemmler et al., 2009), but show synthetic sickness with stu2 alleles that are involved in error correction.
**Major points:**
Within the framework of this experimental setting, the study as presented is logical and clear. The conclusions regarding the effect of Mps1 in this reconstituted system are overall well supported by the data. I have a couple of major and some minor points that can further improve data interpretation and should therefore be considered:
- In previous publications (e.g. Gutierrez et al., Current Biology 2020), the authors have reported that the Dam1 complex, an established Mps1 substrate, is required for full attachment strength in this system. Are the effects of Mps1-dependent Ndc80 phosphorylation and Dam1 independent from one another? For example would dad1-1 or non Cdk1 phosphorylatable Dam1 complex further reduce the rupture force in ATP? Or does Mps1 phosphorylation affect, for example, Dam1 binding to Ndc80?
Response: To better understand the effects of ATP treatment, we analyzed the levels of Dam1 on the kinetochores after ATP treatment and did not see any change. We will add this data to a supplemental figure. Dam1 clearly makes a major contribution to the strength of the kinetochores because their strength even after ATP-treatment is higher than the rupture force of kinetochores purified from a dad1-1 mutant strain. However, as we report in the paper, blocking the eight Mps1 target sites in the tail of Ndc80 was sufficient to block the effect of ATP, so it is unlikely that phosphorylation of the Dam1 complex by Mps1 makes a major contribution to the ATP-dependent kinetochore weakening in vitro. We think Dam1 phosphorylation by Aurora B probably contributes independently to error correction, because the dam1-3D mutant, carrying phospho-mimetic substitutions in three Aurora B sites, is synthetically lethal when combined with the ndc80-8D phospho-mimetic mutant in eight Mps1 sites. We will add this genetic interaction data to the revised manuscript to provide additional information about the pathways.
What is the effect of ATP on initial binding events? Are there differences in the fraction of beads that spontaneously attach laterally at the start of the experiment? This may allow to draw conclusions whether any kind of binding or specifically force-generating end-on attachments are affected by ATP.
Response: We did measure a reduction in the fraction of free kinetochore-decorated beads capable of binding microtubules upon exposure to ATP (from 20% binding in the absence of adenosine to 11% in the presence of ATP). This observation suggests that the microtubule-binding activity of the kinetochores, like their rupture strength, is reduced upon exposure to ATP, as reported in the methods, in the "rupture force measurements" section. However, because we worked with a low density of kinetochores on the beads, the initial numbers of beads that spontaneously attached was quite low and free beads capable of binding to microtubules were relatively rare. In addition, when we find a bead already attached to the lattice, we cannot distinguish whether it bound initially to the lattice or instead bound to a tip that then grew beyond the bead. For these reasons, we feel it would be very difficult using our current approach to draw statistically significant conclusions about whether there were ATP-dependent changes in the relative affinities of the kinetochores for lateral versus tip attachments.
Ndc80-8D has low attachment strength, consistent with lowered MT affinity of the phospho-mimetic Ndc80 tail. Interestingly, Supplementary Figure S4B shows that the amount of Cse4 in the pull-down western appears substantially reduced in 8D vs 8A or wt. Is the amount of co-purified inner kinetochore affected in this mutant? This may be an alternative explanation for decreased attachment strength, for example if the fraction of "full" or "complete" kinetochores may be reduced. Could this also happen upon inclusion of ATP?
Response: The reviewer is correct that the level of Cse4 and other inner kinetochore components is slightly reduced in the Ndc80-8D kinetochores, for reasons that are not clear to us. However, the incubation of wild type kinetochores with ATP does not affect the levels of these proteins, suggesting that the weakened rupture strength is not due to reduced levels of these inner kinetochore proteins. We will add the data showing that ATP does not affect levels of inner kinetochore proteins into a supplemental figure to clarify this point.
**Minor points:**
page 13 (heading): "Weakening occurs via phosphorylation...". Probably good to mention what is weakened ("Weakening of kinetochore-microtubule attachments occurs via phosphorylation...".
Response: We will alter the heading as suggested.
page 14/Figure5C: Median Rupture Force for Ndc80-8D is 4.8 pN according to the text. In the graph it looks like >5 pN.
Response: We thank the reviewer for noticing this mistake and will correct the median rupture force to 5.6 pN.
page 23: comma missing between T21 S37 and T47 (should be T21, S37 and T47)
Response: We thank the reviewer for noticing this omission and will correct it.
page 24/25: different spelling of G1 (sometimes with subscript)
Response: We thank the reviewer for noticing this inconsistency and will correct all to be G1.
page 24/25: ug instead of µg
Response: Thanks. We will fix this mistake.
page 28: Figure 5B instead of Figure 5A
Response: Thanks for noticing this mistake. We will correct this.
Figure 6A: Lambda-Phosphatase treatment for 20 minutes according to figure legend and 30 minutes according to Material and Methods section.
Response: The material and methods section specified a 20-minute incubation with phosphatase, in agreement with the figure legend. We believe the reviewer might have accidentally confused the time value with the temperature, which was 30 degrees.
Figure 6E: One should not draw any conclusions from the anti-phospho T47 blot here, the quality is simply too poor to allow a statement regarding an mps1-1 effect
Response: While the immunoblots with the T74 phospho-specific antibody are not as clean as many standard antibodies, we have reproduced the results multiple times and therefore feel comfortable concluding that there is a decrease in signal that is Mps1-dependent.
Figure 6: Labelling T47P misleading (Proline substitution?, use pT47 instead)
Response: We will change the labeling on this figure, as suggested, from T74P to pT74. To be consistent, we will also change this nomenclature in the text.
Figure 6F: Make clear in the labelling that a stu2-AID background is used here, makes it easier to understand why Auxin is used here.
Response: We will change the labeling, as suggested, to include the genotype of stu2-AID in the figure.
how specific is reversine for yeast Mps1? I have not seen any data on this in previous publications.
Response: Reversine is not necessarily specific for Mps1. However, the only kinase activity that co-purifies with the isolated kinetochores is from Mps1, so reversine should inhibit only Mps1 in our in vitro experiments. Nevertheless, to further address this concern, we will include optical trapping results using mps1-1 mutant kinetochores in the revised manuscript. We have already performed these additional experiments and found that mps1-1 kinetochores do not undergo ATP-dependent weakening, strongly reinforcing our conclusion that Mps1 is the major kinase involved.
additional genetic interactions might be informative, if Ndc80-8D has weakened attachments, it may have synthetic effects with other mutants (dam1?), conversely, ndc80-8A may show genetic interactions with ipl1 alleles, for example.
Response: We agree that the ndc80 phospho-mutant alleles might have genetic interactions with other mutants. Consistent with this prediction, we have found that ndc80-8D is synthetically lethal when combined with the dam1-3D mutant in three Ipl1 sites. As mentioned above, we will add this data into the revised text. We will also perform additional genetic interaction experiments with ipl1 and mps1 alleles and add any additional interactions we discover into the revised text.
Reviewer #1 (Significance (Required)):
The study adds to the characterization of the effects of Mps1 kinase on kinetochore-microtubule attachments and characterizes the cellular phenotypes of non-Mps1 phosphorylatable Ndc80 mutants. The major conceptual point that Mps1 phosphorylation can weaken kinetochore-microtubule interactions and thereby contributes to error correction in a manner similar to Ipl1 has previously been made in the literature. Maure et al., (Tanaka lab, 2007, Current Biology) have characterized the effects of mps1 mutant alleles on biorientation of authentic chromosomes and on replicated/unreplicated mini-chromosomes. In particular the experiments with unreplicated mini-chromosomes have revealed less frequent detachment in mps1 mutants, demonstrating that Mps1 activity is required to release attachments that are not under tension.
Another benefit of this study is that it puts the Kemmler 2009 EMBO J. paper into perspective and corrects some of it claims. In particular the notion of sustained checkpoint activation in the Mps1 phospho-mimetic Ndc80-14D mutant, whose lethality was claimed to be rescued by checkpoint deletion. It is confirmed here that the allele is lethal but cannot be alleviated by simultaneous checkpoint deletion. Conversely, the Ndc80-14A mutant is shown to have a functional checkpoint. One could argue that since the publication of the Kemmler paper, the idea of requirement of Mps1 phosphorylation on Ndc80 for checkpoint activity has not gained any traction in the field, but it's still useful for the field to put some of these earlier claims into perspective. The paper will therefore be interesting to researchers working on mechanisms of chromosome segregation and error correction.
From my background I cannot comment on technical details of the biophysical force spectroscopy experiments (laser trapping), but I have no reason to doubt that the authors accurately report their findings.
Response: We sincerely thank the reviewer for their careful reading, helpful comments, and enthusiasm for our manuscript.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
This paper focusses on the mechanisms underlying chromosome biorientation in mitosis, an essential process that warrants equal chromosome segregation to the dividing cells. Correction of improper kinetochore-microtubule attachments relies on two conserved protein kinases, Aurora B and Mps1, that detach kinetochores that are not under tension in order to provide them with a second opportunity to establish bipolar connections. In vivo, Aurora B and Mps1 have intertwined functions and share some common targets. For this reason, despite the large body of literature on the subject, their precise roles in chromosome biorientation have been difficult to tease apart.
The authors take advantage of an in vitro reconstitution assay that they previously published (Akyioshi et al., 2010) to identify the critical target(s) of Mps1 in weakening kinetochore-microtubule connections. The assay uses kinetochore particles purified from budding yeast cells that bear Mps1 but are notably deprived of Aurora B. Upon addition of ATP to activate the co-purified kinases (e.g. Mps1), kinetochores are added to coverslip-anchored microtubules to which they attach laterally. Through a laser trap, kinetochores are brought to the microtubule plus-end and pulled with increasing force until the kinetochore detaches, which allows measurements of the average rupture forces that reflect the strength of the attachments. The approach is straightforward and potentially very powerful, first because it provides a simplified experimental set-up in comparison to the cellular context, and second because it directly measures the impact of protein phosphorylation on the strength of attachments.
The authors convincingly show that Mps1-dependent phosphorylation of the N-terminal part of Ndc80 significantly weakens the strength of kinetochore-microtubule attachments in vitro, while phosphorylation of other known Mps1 targets, such as Spc105, does not seem to have an effect. Eight phosphorylation sites in Ndc80, which were previously identified as Mps1-dependent phosphorylation sites (Kemmler et al., 2009), are shown to be critical to destabilise kinetochore-microtubule attachments in the in vitro reconstitution assays. The authors also present evidence for a moderate involvement of Ndc80 phosphorylation by Mps1 in correcting improper attachments in vivo, suggesting that additional mechanisms are physiologically relevant for error correction.
The experiments are mostly well designed, the data are solid and support the main conclusions. However, to my opinion additional experiments could be performed, as outlined below, to strengthen the physiological relevance of the main findings and corroborate some of the conclusions.
**Major points:**
- Given the partially overlapping function of Mps1 and Ipl1 (Aurora B) in error correction, the ndc80-8A mutant should display synthetic growth and chromosome mis-segregation defects with ipl1 temperature-sensitive alleles. Conversely, the ndc80-8D mutant should suppress the lethality at high temperatures of mps1-3 mutant cells, which were recently shown to be defective in chromosome biorientation (Benzi et al., 2020). Finally, chromosome mono-orientation could become apparent in ndc80-8A cells upon a transient treatment with microtubule-depolymerising drugs, which should amplify the cellular need for error correction.
Response: We agree that further exploration of the possible genetic interactions might help to reinforce the physiological relevance of our main findings. Toward this goal, we will obtain the mps1-3 mutant to determine whether ndc80-8D can suppress its lethality and will add this to the revised manuscript if there is a positive result. As mentioned in response to Reviewer 1, we will add a synthetic lethal interaction between ndc80-8D and a dam1-3D mutant where the Aurora B sites are altered to the revised text. We will also perform additional genetic interactions with ipl1 and mps1 mutants and add any we find into the revision. As requested, we will perform a nocodazole wash out experiment, to determine if ndc80-8A cells show a defect in error correction and add this data to the revision if there is a defect.
The authors show that Mps1-dependent phosphorylation of Ndc80 is not involved in the spindle assembly checkpoint, a conclusion that contradicts a previous report (Kemmler et al., 2009). They also find, in contrast with the same report, that the lethal phenotype of the ndc80-14D phospho-mimetic mutant cannot be rescued by disabling the spindle checkpoint. In my opinion, Kemmler et al. convincingly showed, through a number of different experimental approaches, that ndc80-14D cells die because of spindle checkpoint hyperactivation. Not only deletion of checkpoint genes was shown to rescue the lethality, but re-introduction of a wild type copy of the deleted checkpoint gene reinstated lethality. Thus, the explanation invoked here that spontaneous suppressing mutations could underlie the viability of ndc80-14D SAC-deficient mutants is not consistent with the published observations. A thorough examination by the authors of the phenotype of ndc80-14D cells in their hands should be carried out to support these conflicting conclusions. If authors find that ndc80-14D cells actually die because of chromosome mono-orientation, then this would highlight an important function for some or all the six additional phosphorylation sites, relative to the ndc80-8D mutant, for chromosome biorientation in vivo.
Response: We were unable to reproduce the data that deletion of the spindle checkpoint suppresses lethality of the ndc80-14Dmutant, so it remains unclear why our results differ from those of the Kemmler paper. However, we note that re-introducing a wild-type checkpoint gene via transformation and restoring lethality to the ndc80-14D cells does not necessarily mean there were no suppressors. While that is one possible interpretation, another possibility is that there was a suppressor mutation in the viable ndc80-14D cells that also required the lack of the checkpoint to live. Kemmler and co-workers selected for viability on FOA media and never backcrossed those viable strains to show that they could regenerate the double mutant through a cross with the expected segregation pattern of two mutations, which would have been a more rigorous demonstration that the viability was specifically due to ndc80-14D and the checkpoint mutation. Instead, they transformed a wild-type copy of the checkpoint gene back into the strain that was selected for growth on FOA and showed that it reverted the phenotype. This approach cannot rule out a suppressor mutation that fails to suppress in the presence of an active checkpoint. Therefore, in our opinion, the Kemmler paper does not make an entirely convincing case that the ndc80-14D cells die because of spindle checkpoint hyperactivation.
To further analyze the phenotype of ndc80-14D cells, we have constructed an Ndc80-AID ndc80-14D strain and added auxin, to deplete the wild-type copy of Ndc80. In agreement with the findings of Kemmler et al., this did trigger the spindle assembly checkpoint. However, when we made an Ndc80-AID ndc80-14D mad2 strain and analyzed segregation, we found that chromosome 8 missegregated in 28% of the cells compared to 2% of control cells. This observation suggests that there is a kinetochore defect in these cells that may have triggered the checkpoint and is inconsistent with the mutant solely activating the checkpoint in the absence of any other kinetochore defect. In addition, the levels of Ndc80-14D as well as Mps1 were altered on the mutant kinetochores. The combination of these defects strongly suggests that the ndc80-14D mutant alters kinetochore function in addition to leading to constitutive checkpoint signaling. Because our manuscript is mainly focused on phosphorylation of the Mps1 target sites within the N-terminal tail, we do not plan to add this data involving many additional sites, including Ipl1 target sites and sites on the CH domains of Ndc80, into the current manuscript. We will further pursue the other phosphorylation sites in the future.
The conclusion that Spc105 phosphorylation by Mps1 is not required for the Mps1-mediated weakening of kinetochore attachments in vitro is based on the comparison between kinetochore particles bearing wild type, untagged Spc105 and particles bearing non-phosphorylatable Spc105-6A tagged at the C-terminus with twelve myc epitopes. Thus, the presence of the tag could obliterate the effects of the mutations in the phosphorylation sites by destabilising kinetochore-microtubule attachments in the presence of ATP. Consistent with this conclusion, Spc105-6A-12myc-bearing kinetochores withstand lower rupture forces than Spc105-bearing kinetochores upon ATP addition. Furthermore, Spc105-6A-12myc kinetochore particles show an interacting protein at MW above 150 KD that is not present in wild type particles (Fig. S2A), suggesting that either the tag or the mutations might affect kinetochore composition. Thus, this set of experiments should be repeated using Spc105-6A kinetochore particles lacking the tag.
Response: If we understand correctly, the reviewer is suggesting that the myc tag on Spc105-6A could cause an ATP-dependent effect on kinetochore strength. While this is formally possible, it seems highly unlikely to us, for two reasons: First, a myc tag is not expected to bind nucleotides, and while it can sometimes have a general effect on protein stability or interfere with protein-protein interactions, we are not aware of any evidence for a myc tag directly causing an ATP-dependent effect in vitro. Second, when we measured Spc105-6A kinetochores in control experiments, without adenosine or with ADP, their rupture strengths were high like wild-type kinetochores. The strength of ADP-treated Spc105-6A kinetochores (8.7 pN), for example, was statistically indistinguishable from that of ADP-treated wild-type kinetochores (8.7 pN, p = 0.27 based on a log-rank test). The wild-type-like behavior of untreated and mock-treated Spc105-6A kinetochores indicates that their composition is not affected in a manner that significantly impacts kinetochore-microtubule strength.
In general, it would have been informative to complement the data presented here with a mass spec analysis of the composition of kinetochore particles, at least for the experiments that are most relevant to the conclusions. For instance, the composition of the Ndc80-8A kinetochore particles is assumed to be similar to that of wild type kinetochores based on gel silver staining (Fig. S4A; note also that ndc80-8A particles are compared to ndc80-8D particles and not to wild type particles). However, the authors previously showed that kinetochore particles purified from dad1-1 mutant cells (affecting the Dam1 complex) have an apparently identical composition to particles purified from wild type cells by silver staining, yet they display significantly lower resistance to the rupture strength in vitro (Akyioshi et al., 2010). What is the status of the Dam1 complex (or other kinetochore subunits) in kinetochores purified from ndc80-8A/-8D or spc105-6A cells relative to wild type kinetochore particles?
Response: We agree that further characterization of the kinetochore particle composition would be valuable and propose to further analyze the composition by purifying wild-type, Ndc80-8A, Ndc80-8D and Spc105-6A kinetochores and performing immunoblotting against the Dam1 complex. In addition, we will analyze the Ndc80-8A and Ndc80-8D kinetochores by mass spectrometry and report a qualitative analysis of the relative amounts of each kinetochore subcomplex in the revised manuscript supplementary data.
**Minor comment:**
I believe that the right reference for the sentence in the Discussion "If Aurora B is defective, for example, the opposing phosphatase PP1 prematurely localizes to kinetochores" is Liu et al. 2010.
Response: We had cited the reference showing this effect in yeast, since our work was performed in yeast. We will also add the Liu et al paper, which showed the same result in human cells.
Reviewer #2 (Significance (Required)):
Although the experiments are well designed and the conclusions are mainly supported by the data, the question arises as to what extent the in vitro assays recapitulate, at least partly, what happens in vivo. An emblematic example is the involvement of Spc105 in the error correction pathway. The Biggins lab previously showed that Spc105 phosphorylation by Mps1 and subsequent Bub1 recruitment is not only essential for the spindle assembly checkpoint, but is also crucial for chromosome segregation in vivo, as shown by slow-growth phenotype and aneuploidy of the spc105-6A non-phosphorylatable mutant (London et al., 2012). Additionally, a recent paper showed that Spc105 is a crucial Mps1 target in chromosome biorientation (Benzi et al., 2020).
In sharp contrast, the ndc80-8A mutant, which in vitro completely erases the ability of Mps1 to destabilise kinetochore-microtubule attachments, displays no growth defects in otherwise wild type cells and only modestly enhances chromosome mis-segregation in a mutant affecting an intrinsic correction pathway (stu2ccΔ). The N-terminal part of Ndc80 (aa 1-116) containing the aforementioned eight phosphorylation sites can even be deleted altogether without any consequence on cell viability (Kemmler et al., 2009). Thus, although the in vitro assays presented here produced clear-cut and reproducible results, their physiological relevance in vivo remains unclear.
Left apart this criticism, the manuscript has several merits outlined above and will be of interest for people working in the fields of chromosome segregation, kinetochore assembly, spindle assembly checkpoint, etc.
Expertise of this reviewer: mitosis and related checkpoints
Response: We are grateful to the reviewer for carefully reading our manuscript and detailing their concerns. We agree that it can be challenging to establish the physiological relevance of experiments performed in vitro. However, our in vitro approach allowed the effects of Mps1 specifically on kinetochore-microtubule attachment strength to be disentangled from its numerous other effects in vivo. In our view, the relatively mild phenotypes associated with mutants in the Mps1 phosphorylation sites on the Ndc80 tail are consistent with similarly mild phenotypes of mutants in the Aurora B phosphorylation sites on the Ndc80 tail. In both cases, this appears to be due to additional error correction pathways that compensate in vivo.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
Sarangapani, Koch, Nelson et al. applied a combination of in vitro biophysical assays with purified kinetochore particles and in vivo analyses to investigate the contribution of Mps1 kinase to kinetochore-microtubule (KT-MT) attachment stability and error correction.
The manuscript is well written and the authors nicely highlight the facts that 1) the focus of the field has long been on the contribution of Aurora kinases (Ipl1 in budding yeast) to attachment stability and error correction, and 2) it has been difficult to assess the relative contributions of Aurora versus Mps1 kinases in cell-based experiments. The authors note that their KT particle assay is uniquely positioned to address this gap in our understanding and to specifically isolate the contribution of Mps1 to attachment stability in vitro. The findings are well-presented and quite convincing although I have several comments that should be addressed to strengthen the central conclusion that this work has isolated the contribution of Mps1 in their assays.
**Major points:**
1) I think it is important to note that reversine is not specific for Mps1 kinase - although it is typically presented as such in the field. It was initially identified as an Aurora kinase inhibitor (IC50: ~25nM (Aurora B) - 900nM (Aurora A)) that turned out be an even more potent Mps1 inhibitor (IC50 ~6nM). I have concerns that the in vitro assays were done with 5 uM reversine - a concentration so high that it could certainly inhibit any Ipl1 that is present (see comment 3 below) and possibly even inhibit Bub1 activity as Santaguida et al. (JCB, 2010) measured an IC50 >1uM for Bub1 inhibition. It is important to complement/confirm the chemical inhibitor experiment by repeating the rupture assays +/- ATP in KT particles purified from the mps1-1 strain (shown in Figure 6).
Response: We agree that reversine is not necessarily specific for Mps1 and this concern was also brought up by Reviewer 1. Because Mps1 is the only kinase activity that co-purifies with the isolated kinetochore particles, we expect reversine to inhibit only Mps1 in our in vitro assays. However, to further address this point, we will add rupture force assays using kinetochores purified from mps1-1 mutant cells to the revised manuscript. We have already performed these experiments and they confirm that kinetochores lacking Mps1 do not undergo ATP-dependent weakening. We did not put this data into the original submission because the experiment needs to be performed differently due to altered Dam1 levels. But we will clarify the changes in the materials and methods and add the data to a supplementary figure.
2) If the ATP-mediated reduction on rupture force is lost in the mps1-1 KT particles, which will also lack Bub1 kinase, then preserving the ATP-dependent reduction in rupture force from KT particles purified from the Bub1delta mutant strain would be strong evidence that the contribution of Mps1 kinase has been disentangled from other kinases in this assay.
Response: Although Mps1 recruits Bub1, we think it is unlikely that we are assaying Bub1 kinase activity in our in vitroexperiments. We cannot detect Bub1 activity on the purified kinetochores using a sensitive radioactive kinase assay (London et al, Curr Bio 2011), and the levels of Bub1 in our kinetochore purifications are very low (for example, see Akiyoshi et al, Nature, 2010). However, we agree with the reviewer that this caveat should be mentioned and will add this point to the revised text for clarity.
3) Recent work has shown that Sli15-Ipl1 interacts with and is recruited to KTs by the COMA complex (Rodriguez et al., Curr Biol, 2019 and Fischbock-Halwachs et al., eLife 2019) and that this population of Ipl1 is important for accurate chromosome segregation as also shown 10 years prior by Knockleby and Vogel (Cell Cycle, 2009). I realize that this group previously showed (London et al., Curr Biol, 2012) that phosphorylation of KT particles was not affected when purified from the ipl1-321 mutants, but in light of the recent findings how sure are the authors that there is not any Sli15-Ipl1 in the preparations? I think commenting on this would be worthwhile.
Response: We have not detected Ipl1 or Sli15 in the numerous mass spectrometry experiments we have performed on the kinetochore purifications. In addition, we have been separately assaying the effects of Ipl1 phosphorylation on kinetochores for another project (de Regt, https://doi.org/10.1101/415992), which independently confirmed that the only detectable kinase activity in our kinetochore purifications is Mps1. We will add this additional reference to the manuscript.
4) Since the interplay between Mps1 and Aurora B are central to this story, the authors should expand upon the sentence on page 5 reading "While there is some evidence that Mps1 regulates Aurora B activity (Jelluma et al., 2010; Saurin et al., 2011; Tighe et al., 2008), significant data suggests it has an independent role in error correction and acts downstream of Aurora B (Hewitt et al., 2010; Maciejowski et al., 2010; Maure et al., 2007; Meyer et al., 2013; Santaguida et al., 2010)." I am not entirely convinced that the in vivo experiments presented here differentiate as to whether Mps1 is upstream from Ipl1 or whether they are acting independently? For example, phosphorylation of T74 looks to be completely lost in figure 6E (although it's difficult to tell since the blot for T74P is very smeary). If they are acting independently in error correction then Ipl1 should still be able to phosphorylate T74 in this condition. However, if the P-T74 really is lost completely in the mcd1-1 cells then this suggests to me that Ipl1 is downstream of Mps1 in this live cell error correction assay.
Response: We thank the reviewer for bringing this to our attention. We did not mean to imply that Mps1 is downstream from Aurora B in budding yeast and were intending only to summarize findings from the literature regarding other organisms. We will revise this section of the text to make that point clearer, and we agree that the order of events remains unresolved. In addition, we will note that Mps1 does not eliminate the phosphorylation detected by the T74 antibody in the revision, to avoid misconceptions about the order of events.
**Other points:**
1) On p.8 "a median strength of 7.5 pN, similar to untreated and ADP-treated kinetochores". Similar is vague so I'm curious as to whether there a statistically significant difference between this and the 9.8 pN and 8.7 pN measured in the other conditions. If so this could be explained by partial dephosphorylation with the phosphatase.
Response: The quoted phrase refers to the 7.5-pN strength measured when λ-phosphatase was included together with ATP (data from Fig. 1D and Supp. Fig. S1B). P-values computed from comparisons of survival plots using the log-rank test show that this strength was not significantly different from the ADP-treated wild-type (8.7 pN, p = 0.06), nor was it significantly different from the ADP- and MnCl2-treated wild-type (8.1 pN, p = 0.35). However, it was barely significantly different from MnCl2-treated wild-type (8.6 pN, p = 0.03), and it was more significantly different from untreated wild-type (9.8 pN, p = 0.0007). With the revised manuscript, we will include a supplemental table with p-values computed from log-rank tests for all the key statistical comparisons, including those mentioned here.
2) On p.19 the authors note that Aurora A phosphorylates Ndc80 tail during mitosis. Ye et al. (Curr Biol, 2015) also showed that Aurora A can phosphorylate Aurora B sites and that this activity "converges" at the tail to weaken attachments during error correction.
Response: We will add the reference and thank the reviewer for pointing out this omission.
3) Optional: I am curious as to whether the addition of ATP to the Ndc80-8D particles further reduces the rupture force. If so then other sites may also be in play.
Response: We agree this is an interesting question but we have not yet performed those assays and agree it might be worthwhile for a future study.
4) Please comment on why MnCl2 is used in the rupture assays in Figure S1. I saw no mention of this in the main text.
Response: We include MnCl2 in the assay because it is required for phosphatase activity and will add this point to the legend of supplementary Figure S1.
5) Consider moving S2 A and B to Figure 3 C and D. This is an interesting result and would go well in the main figure next to the significantly reduced rupture force measurements for the 6A mutant so the reader doesn't have to dig into the supplemental for the data providing this reasonable explanation for the rupture force result.
Response: We thank the reviewer for this suggestion and will move S2A and S2B into Figure 3.
Reviewer #3 (Significance (Required)):
The significance of this relates to focusing on an important phenomenon - error correction - and in looking beyond the traditional focus of the field on Aurora kinases to Mps1 kinase, which is largely implicated in checkpoint signaling. Disentangling the contributions of these two players is an important advance.
The work will be of interest to audiences interested in: kinases, cell division, checkpoints, kinetochore biology, biophysics
The above areas of interest overlap with my expertise.
Response: We thank the reviewer for their enthusiasm for our experiments that help distinguish kinase activities and thus contribute to understanding the process of error correction.
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Referee #3
Evidence, reproducibility and clarity
Sarangapani, Koch, Nelson et al. applied a combination of in vitro biophysical assays with purified kinetochore particles and in vivo analyses to investigate the contribution of Mps1 kinase to kinetochore-microtubule (KT-MT) attachment stability and error correction. The manuscript is well written and the authors nicely highlight the facts that 1) the focus of the field has long been on the contribution of Aurora kinases (Ipl1 in budding yeast) to attachment stability and error correction, and 2) it has been difficult to assess the relative contributions of Aurora versus Mps1 kinases in cell-based experiments. The authors note that their KT particle assay is uniquely positioned to address this gap in our understanding and to specifically isolate the contribution of Mps1 to attachment stability in vitro. The findings are well-presented and quite convincing although I have several comments that should be addressed to strengthen the central conclusion that this work has isolated the contribution of Mps1 in their assays.
Major points:
1) I think it is important to note that reversine is not specific for Mps1 kinase - although it is typically presented as such in the field. It was initially identified as an Aurora kinase inhibitor (IC50: ~25nM (Aurora B) - 900nM (Aurora A)) that turned out be an even more potent Mps1 inhibitor (IC50 ~6nM). I have concerns that the in vitro assays were done with 5 uM reversine - a concentration so high that it could certainly inhibit any Ipl1 that is present (see comment 3 below) and possibly even inhibit Bub1 activity as Santaguida et al. (JCB, 2010) measured an IC50 >1uM for Bub1 inhibition. It is important to complement/confirm the chemical inhibitor experiment by repeating the rupture assays +/- ATP in KT particles purified from the mps1-1 strain (shown in Figure 6).
2) If the ATP-mediated reduction on rupture force is lost in the mps1-1 KT particles, which will also lack Bub1 kinase, then preserving the ATP-dependent reduction in rupture force from KT particles purified from the Bub1delta mutant strain would be strong evidence that the contribution of Mps1 kinase has been disentangled from other kinases in this assay.
3) Recent work has shown that Sli15-Ipl1 interacts with and is recruited to KTs by the COMA complex (Rodriguez et al., Curr Biol, 2019 and Fischbock-Halwachs et al., eLife 2019) and that this population of Ipl1 is important for accurate chromosome segregation as also shown 10 years prior by Knockleby and Vogel (Cell Cycle, 2009). I realize that this group previously showed (London et al., Curr Biol, 2012) that phosphorylation of KT particles was not affected when purified from the ipl1-321 mutants, but in light of the recent findings how sure are the authors that there is not any Sli15-Ipl1 in the preparations? I think commenting on this would be worthwhile.
4) Since the interplay between Mps1 and Aurora B are central to this story, the authors should expand upon the sentence on page 5 reading "While there is some evidence that Mps1 regulates Aurora B activity (Jelluma et al., 2010; Saurin et al., 2011; Tighe et al., 2008), significant data suggests it has an independent role in error correction and acts downstream of Aurora B (Hewitt et al., 2010; Maciejowski et al., 2010; Maure et al., 2007; Meyer et al., 2013; Santaguida et al., 2010)." I am not entirely convinced that the in vivo experiments presented here differentiate as to whether Mps1 is upstream from Ipl1 or whether they are acting independently? For example, phosphorylation of T74 looks to be completely lost in figure 6E (although it's difficult to tell since the blot for T74P is very smeary). If they are acting independently in error correction then Ipl1 should still be able to phosphorylate T74 in this condition. However, if the P-T74 really is lost completely in the mcd1-1 cells then this suggests to me that Ipl1 is downstream of Mps1 in this live cell error correction assay.
Other points:
1) On p.8 "a median strength of 7.5 pN, similar to untreated and ADP-treated kinetochores". Similar is vague so I'm curious as to whether there a statistically significant difference between this and the 9.8 pN and 8.7 pN measured in the other conditions. If so this could be explained by partial dephosphorylation with the phosphatase.
2) On p.19 the authors note that Aurora A phosphorylates Ndc80 tail during mitosis. Ye et al. (Curr Biol, 2015) also showed that Aurora A can phosphorylate Aurora B sites and that this activity "converges" at the tail to weaken attachments during error correction.
3) Optional: I am curious as to whether the addition of ATP to the Ndc80-8D particles further reduces the rupture force. If so then other sites may also be in play.
4) Please comment on why MnCl2 is used in the rupture assays in Figure S1. I saw no mention of this in the main text.
5) Consider moving S2 A and B to Figure 3 C and D. This is an interesting result and would go well in the main figure next to the significantly reduced rupture force measurements for the 6A mutant so the reader doesn't have to dig into the supplemental for the data providing this reasonable explanation for the rupture force result.
Significance
The significance of this relates to focusing on an important phenomenon - error correction - and in looking beyond the traditional focus of the field on Aurora kinases to Mps1 kinase, which is largely implicated in checkpoint signaling. Disentangling the contributions of these two players is an important advance.
The work will be of interest to audiences interested in: kinases, cell division, checkpoints, kinetochore biology, biophysics
The above areas of interest overlap with my expertise.
-
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Referee #2
Evidence, reproducibility and clarity
This paper focusses on the mechanisms underlying chromosome biorientation in mitosis, an essential process that warrants equal chromosome segregation to the dividing cells. Correction of improper kinetochore-microtubule attachments relies on two conserved protein kinases, Aurora B and Mps1, that detach kinetochores that are not under tension in order to provide them with a second opportunity to establish bipolar connections. In vivo, Aurora B and Mps1 have intertwined functions and share some common targets. For this reason, despite the large body of literature on the subject, their precise roles in chromosome biorientation have been difficult to tease apart.
The authors take advantage of an in vitro reconstitution assay that they previously published (Akyioshi et al., 2010) to identify the critical target(s) of Mps1 in weakening kinetochore-microtubule connections. The assay uses kinetochore particles purified from budding yeast cells that bear Mps1 but are notably deprived of Aurora B. Upon addition of ATP to activate the co-purified kinases (e.g. Mps1), kinetochores are added to coverslip-anchored microtubules to which they attach laterally. Through a laser trap, kinetochores are brought to the microtubule plus-end and pulled with increasing force until the kinetochore detaches, which allows measurements of the average rupture forces that reflect the strength of the attachments. The approach is straightforward and potentially very powerful, first because it provides a simplified experimental set-up in comparison to the cellular context, and second because it directly measures the impact of protein phosphorylation on the strength of attachments.
The authors convincingly show that Mps1-dependent phosphorylation of the N-terminal part of Ndc80 significantly weakens the strength of kinetochore-microtubule attachments in vitro, while phosphorylation of other known Mps1 targets, such as Spc105, does not seem to have an effect. Eight phosphorylation sites in Ndc80, which were previously identified as Mps1-dependent phosphorylation sites (Kemmler et al., 2009), are shown to be critical to destabilise kinetochore-microtubule attachments in the in vitro reconstitution assays. The authors also present evidence for a moderate involvement of Ndc80 phosphorylation by Mps1 in correcting improper attachments in vivo, suggesting that additional mechanisms are physiologically relevant for error correction.
The experiments are mostly well designed, the data are solid and support the main conclusions. However, to my opinion additional experiments could be performed, as outlined below, to strengthen the physiological relevance of the main findings and corroborate some of the conclusions.
Major points:
- Given the partially overlapping function of Mps1 and Ipl1 (Aurora B) in error correction, the ndc80-8A mutant should display synthetic growth and chromosome mis-segregation defects with ipl1 temperature-sensitive alleles. Conversely, the ndc80-8D mutant should suppress the lethality at high temperatures of mps1-3 mutant cells, which were recently shown to be defective in chromosome biorientation (Benzi et al., 2020). Finally, chromosome mono-orientation could become apparent in ndc80-8A cells upon a transient treatment with microtubule-depolymerising drugs, which should amplify the cellular need for error correction.
- The authors show that Mps1-dependent phosphorylation of Ndc80 is not involved in the spindle assembly checkpoint, a conclusion that contradicts a previous report (Kemmler et al., 2009). They also find, in contrast with the same report, that the lethal phenotype of the ndc80-14D phospho-mimetic mutant cannot be rescued by disabling the spindle checkpoint. In my opinion, Kemmler et al. convincingly showed, through a number of different experimental approaches, that ndc80-14D cells die because of spindle checkpoint hyperactivation. Not only deletion of checkpoint genes was shown to rescue the lethality, but re-introduction of a wild type copy of the deleted checkpoint gene reinstated lethality. Thus, the explanation invoked here that spontaneous suppressing mutations could underlie the viability of ndc80-14D SAC-deficient mutants is not consistent with the published observations. A thorough examination by the authors of the phenotype of ndc80-14D cells in their hands should be carried out to support these conflicting conclusions. If authors find that ndc80-14D cells actually die because of chromosome mono-orientation, then this would highlight an important function for some or all the six additional phosphorylation sites, relative to the ndc80-8D mutant, for chromosome biorientation in vivo.
- The conclusion that Spc105 phosphorylation by Mps1 is not required for the Mps1-mediated weakening of kinetochore attachments in vitro is based on the comparison between kinetochore particles bearing wild type, untagged Spc105 and particles bearing non-phosphorylatable Spc105-6A tagged at the C-terminus with twelve myc epitopes. Thus, the presence of the tag could obliterate the effects of the mutations in the phosphorylation sites by destabilising kinetochore-microtubule attachments in the presence of ATP. Consistent with this conclusion, Spc105-6A-12myc-bearing kinetochores withstand lower rupture forces than Spc105-bearing kinetochores upon ATP addition. Furthermore, Spc105-6A-12myc kinetochore particles show an interacting protein at MW above 150 KD that is not present in wild type particles (Fig. S2A), suggesting that either the tag or the mutations might affect kinetochore composition. Thus, this set of experiments should be repeated using Spc105-6A kinetochore particles lacking the tag.
- In general, it would have been informative to complement the data presented here with a mass spec analysis of the composition of kinetochore particles, at least for the experiments that are most relevant to the conclusions. For instance, the composition of the Ndc80-8A kinetochore particles is assumed to be similar to that of wild type kinetochores based on gel silver staining (Fig. S4A; note also that ndc80-8A particles are compared to ndc80-8D particles and not to wild type particles). However, the authors previously showed that kinetochore particles purified from dad1-1 mutant cells (affecting the Dam1 complex) have an apparently identical composition to particles purified from wild type cells by silver staining, yet they display significantly lower resistance to the rupture strength in vitro (Akyioshi et al., 2010). What is the status of the Dam1 complex (or other kinetochore subunits) in kinetochores purified from ndc80-8A/-8D or spc105-6A cells relative to wild type kinetochore particles?
Minor comment:
I believe that the right reference for the sentence in the Discussion "If Aurora B is defective, for example, the opposing phosphatase PP1 prematurely localizes to kinetochores" is Liu et al. 2010.
Significance
Although the experiments are well designed and the conclusions are mainly supported by the data, the question arises as to what extent the in vitro assays recapitulate, at least partly, what happens in vivo. An emblematic example is the involvement of Spc105 in the error correction pathway. The Biggins lab previously showed that Spc105 phosphorylation by Mps1 and subsequent Bub1 recruitment is not only essential for the spindle assembly checkpoint, but is also crucial for chromosome segregation in vivo, as shown by slow-growth phenotype and aneuploidy of the spc105-6A non-phosphorylatable mutant (London et al., 2012). Additionally, a recent paper showed that Spc105 is a crucial Mps1 target in chromosome biorientation (Benzi et al., 2020).
In sharp contrast, the ndc80-8A mutant, which in vitro completely erases the ability of Mps1 to destabilise kinetochore-microtubule attachments, displays no growth defects in otherwise wild type cells and only modestly enhances chromosome mis-segregation in a mutant affecting an intrinsic correction pathway (stu2ccΔ). The N-terminal part of Ndc80 (aa 1-116) containing the aforementioned eight phosphorylation sites can even be deleted altogether without any consequence on cell viability (Kemmler et al., 2009). Thus, although the in vitro assays presented here produced clear-cut and reproducible results, their physiological relevance in vivo remains unclear.
Left apart this criticism, the manuscript has several merits outlined above and will be of interest for people working in the fields of chromosome segregation, kinetochore assembly, spindle assembly checkpoint, etc.
Expertise of this reviewer: mitosis and related checkpoints
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Referee #1
Evidence, reproducibility and clarity
The authors use a combination of Dsn1-Flag kinetochore purification from yeast extracts and laser trapping experiments (as in a number of previous studies), to study the effect of Mps1-dependent phosphorylation on reconstituted kinetochore-microtubule attachments in vitro. They complement this analysis with genetic experiments characterizing the effects of non-Mps1 phosphorylatable mutants on checkpoint activity and chromosome segregation in yeast. The authors had previously shown that Mps1 is the major kinase activity that copurifies with Dsn1-Flag in their purification scheme. They now investigate the effect of adding ATP and thereby allowing Mps1 phosphorylation in the reconstituted system. They show that addition of ATP decreases the rupture force of kinetochore-microtubule attachments, meaning it weakens the strength of the attachment. This effect can be negated either by inhibiting Mps1 with reversine, or by providing kinetochores in which the Mps1 phosphorylation sites on Ndc80 (most of them in the N-terminal tail) have been mutated to alanine. Thus, similar to the activity of Ipl1, Mps1 phosphorylation of the Ndc80 N-tail (which is known to be important for for full MT affinity) weakens kinetochore-microtubule attachments.
Cellular experiments demonstrate that non-Mps1 phosphorylatable Ndc80 14-A mutants have a functional mitotic checkpoint (contrary to previous claims by Kemmler et al., 2009), but show synthetic sickness with stu2 alleles that are involved in error correction.
Major points:
Within the framework of this experimental setting, the study as presented is logical and clear. The conclusions regarding the effect of Mps1 in this reconstituted system are overall well supported by the data. I have a couple of major and some minor points that can further improve data interpretation and should therefore be considered:
- In previous publications (e.g. Gutierrez et al., Current Biology 2020), the authors have reported that the Dam1 complex, an established Mps1 substrate, is required for full attachment strength in this system. Are the effects of Mps1-dependent Ndc80 phosphorylation and Dam1 independent from one another? For example would dad1-1 or non Cdk1 phosphorylatable Dam1 complex further reduce the rupture force in ATP? Or does Mps1 phosphorylation affect, for example, Dam1 binding to Ndc80?
- What is the effect of ATP on initial binding events? Are there differences in the fraction of beads that spontaneously attach laterally at the start of the experiment? This may allow to draw conclusions whether any kind of binding or specifically force-generating end-on attachments are affected by ATP.
- Ndc80-8D has low attachment strength, consistent with lowered MT affinity of the phospho-mimetic Ndc80 tail. Interestingly, Supplementary Figure S4B shows that the amount of Cse4 in the pull-down western appears substantially reduced in 8D vs 8A or wt. Is the amount of co-purified inner kinetochore affected in this mutant? This may be an alternative explanation for decreased attachment strength, for example if the fraction of "full" or "complete" kinetochores may be reduced. Could this also happen upon inclusion of ATP?
Minor points:
page 13 (heading): "Weakening occurs via phosphorylation...". Probably good to mention what is weakened ("Weakening of kinetochore-microtubule attachments occurs via phosphorylation...".
page 14/Figure5C: Median Rupture Force for Ndc80-8D is 4.8 pN according to the text. In the graph it looks like >5 pN.
page 23: comma missing between T21 S37 and T47 (should be T21, S37 and T47)
page 24/25: different spelling of G1 (sometimes with subscript)
page 24/25: ug instead of µg
page 28: Figure 5B instead of Figure 5A
Figure 6A: Lambda-Phosphatase treatment for 20 minutes according to figure legend and 30 minutes according to Material and Methods section.
Figure 6E: One should not draw any conclusions from the anti-phospho T47 blot here, the quality is simply too poor to allow a statement regarding an mps1-1 effect
Figure 6: Labelling T47P misleading (Proline substitution?, use pT47 instead)
Figure 6F: Make clear in the labelling that a stu2-AID background is used here, makes it easier to understand why Auxin is used here.
how specific is reversine for yeast Mps1? I have not seen any data on this in previous publications.
additional genetic interactions might be informative, if Ndc80-8D has weakenend attachments, it may have synthetic effects with other mutants (dam1?), conversely, ndc80-8A may show genetic interactions with ipl1 alleles, for example.
Significance
The study adds to the characterization of the effects of Mps1 kinase on kinetochore-microtubule attachments and characterizes the cellular phenotypes of non-Mps1 phosphorylatable Ndc80 mutants. The major conceptual point that Mps1 phosphorylation can weaken kinetochore-microtubule interactions and thereby contributes to error correction in a manner similar to Ipl1 has previously been made in the literature. Maure et al., (Tanaka lab, 2007, Current Biology) have characterized the effects of mps1 mutant alleles on biorientation of authentic chromosomes and on replicated/unreplicated mini-chromosomes. In particular the experiments with unreplicated mini-chromosomes have revealed less frequent detachment in mps1 mutants, demonstrating that Mps1 activity is required to release attachments that are not under tension.
Another benefit of this study is that it puts the Kemmler 2009 EMBO J. paper into perspective and corrects some of it claims. In particular the notion of sustained checkpoint activation in the Mps1 phospho-mimetic Ndc80-14D mutant, whose lethality was claimed to be rescued by checkpoint deletion. It is confirmed here that the allele is lethal, but cannot be alleviated by simultaneous checkpoint deletion. Conversely, the Ndc80-14A mutant is shown to have a functional checkpoint. One could argue that since the publication of the Kemmler paper, the idea of requirement of Mps1 phosphorylation on Ndc80 for checkpoint activity has not gained any traction in the field, but it's still useful for the field to put some of these earlier claims into perspective. The paper will therefore be interesting to researchers working on mechanisms of chromosome segregation and error correction.
From my background I cannot comment on technical details of the biophysical force spectroscopy experiments (laser trapping), but I have no reason to doubt that the authors accurately report their findings.
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Reply to the reviewers
General comments:
We thank the reviewers for their constructive critique and are pleased they see the results as interesting and of general relevance. We also acknowledge their concerns on the issue of whether all claims are supported by sufficiently strong data. Our careful reading and analysis of the points that are raised suggest there are different reasons for the different cases that are brought up:
- Misunderstandings, due to lack of clarity on our side. Example: When talking about ‘reduced actin’, our wording focussed on the endosome-associated actin (partly out of consideration for the fact the actual measurements we show come from the area around the endosomes, so we did not want to make any stronger claims), even though we should have made it clear that other areas of the cell tip are also affected. This will be addressed by clearer explanations.
Ill-advised wording we chose that is or can be seen as overinterpretation.
Example: ‘anchoring’ of actin at endosomes. We had not intended to infer anything about specific anchoring sites or mechanisms. We should have used a more neutral term, such as ‘associate with’ or accumulate around’ for the description. This and other cases can also be resolved by rewriting and better wording.
Anecdotal evidence or insufficient data.
Example: Images of phalloidin stainings depicting how actin is organized around late endosomes in control embryos. These and other cases will be addressed by adding further examples and additional quantification.
Finally, one suggestion was made for obtaining additional experimental data, which would involve laser ablation. While the experiment would provide an interesting extension of our findings, we will sadly not be in a position to carry it out in the foreseeable future, as explained below. We hope the referees will agree that our now extended discussion addresses the point in question sufficiently to support the conclusions from the experiments we do present.
These and all other points are addressed individually below. We highlighted the corresponding text changes in the manuscript file for the reviewers to identify them more easily.
Detailed responses:
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
**Summary**
Rios-Barrera and Leptin investigate the formation and guidance of the subcellular tube that forms in the terminal cell of the dorsal branches of the Drosophila tracheal system. In previous work the authors documented the presence of late endosomes at the tip of the growing terminal cell, ahead of the forming subcellular tube, which are involved in membrane recycling {Mathew, 2020 #1407}. In this present work they analyze the organization of the actin cytoskeleton in the tip terminal cell, in relation with the late endosomes, and assess the guidance of the subcellular tube. They find that the presence and localization of late endosomes play a role in tube guidance. They also find that late endosomes recruit actin around them, mediated by the activity of the actin polymerization regulator Wash, which is recruited to maturing late endosomes. When Wash activity is decreased, actin around late endosomes is decreased and tube guidance is compromised. Based on this observation, laser ablation experiments of actin ahead of the tube and actin staining at the tip of the terminal cell, the authors propose an exciting model: late endosomes recruit actin, which connects the actin pool of the basal membrane and the actin pool of the apical (subcellular tube) membrane thereby directing tube growth and guidance.
The manuscript is well-written and well-presented, the images and movies are of high quality and the experimental data, which is technically challenging, is very good and sufficiently replicated.
**Major comments:**
- A critical point in the model that the authors put forward (which is also contained in the title and abstract) is that actin organized at late endosomes anchors apical and basal actin cortices. However, there is no clear and conclusive evidence for this. Clear evidence in this direction should be provided to propose it as a mechanism (as it is in the text, particularly in the first sentences of the discussion) and imply it in the title. The authors show endogenous actin around late endosomes and actin fibers at the tip of the terminal branch. However, at the level of resolution presented (Fig 3A,B), it is not possible to determine whether the different actin populations are actually "anchored". I suggest to present stronger data supporting this important conclusion.
In the same direction, it would be critical to show that this anchoring of actin fibers is disturbed when actin enrichment at the late endosome is perturbed (see also point 5).
Actually, the authors show that when Vha or Wash activity are downregulated actin accumulation around the CD4 vesicles decrease. However, this experiment has a few inconveniences. First, it is difficult to determine levels of a construct that is overexpressed (UAS-utr::GFP). Could the authors use phalloidin or an actin antibody to confirm the result?
Second, I find the result difficult to interpret. In the images provided I see a general decrease of actin (UtrGFP) at the tip, not only around the CD4 vesicles (Fig 6D,F) . Are these mutant conditions also affecting the rest of actin pools? If this is the case, can the authors attribute the defects exclusively to the abnormal recruitment of actin to the late endosomes?
Most importantly, the authors should analyze the pattern of actin distribution (labelling endogenous actin) and determine a possible loss of "anchoring" of fibers when late endosome maturation is perturbed.
We understand the referee addresses three issues here, to which we will respond in turn below:
- As already mentioned above, the referee interprets the term ‘anchoring’ in a more specific meaning than we had intended it to have. We obviously have to rephrase.
- A technical critique of the use of an overexpressed construct to visualize actin, which in turn has two sub-points: potential physiological effects on actin, and potentially inaccurate localisation. Both are valid points, but in our view do not undermine our conclusions. We will raise and discuss these concerns in our revised text.
- The specificity of the effects of reducing Vha and Wash of function on actin associated with endosomes versus throughout the growth cone of the cell – a very good point, about which we should have been much clearer and now will be. (a) Considering the use of the term ‘anchoring’, and the referee’s concern over whether we provide the appropriate evidence gave us with a good starting point to re-think what we actually show and how it can be interpreted.
Put in neutral terms, what [we felt] we had shown was an accumulation or enrichment of actin around endosomes that was dependent on proper functioning of Vha and Wash.
We agree that the term ‘anchoring’ cannot be justified by the description of actin localisation alone. The term implies a physical (and perhaps strong or long term) interaction between the endosome and the surrounding actin.
We see a strong enrichment of actin around endosomes, including in experiments in which we use phalloidin to visualize actin (Fig. 3B). The resolution of our images is approximately 200nm so they are able to reveal the very close association. The question is what the mechanistic basis for this closeness is. It is unlikely to be random, as shown by a quantification we have now included (Figure S3C). It is difficult to imagine how it could persist without at least transient physical interaction between the two components. The association is indeed highly dynamic and is constantly being re-established. This must mean that something ‘attracts’ actin to endosomes, most likely a molecule that is itself associated with endosomes. The presence or accessibility of such a molecule depends on the proper maturation of endosomes, as shown by the results of reducing Vha activity. And the ability of actin to associate depends on Wash. Together these findings suggest to us the existence of a (dynamic) molecular link between the endosomes and the actin network.
In order not to give the impression that we are claiming a permanent ‘anchor’, we now use more general terms such as ‘associates’ or ‘accumulates’, but also include the clarification on our thinking in the text. Furthermore, to illustrate a representative range of cases, we will add more examples of late endosomes and the actin meshwork surrounding them (Figure S3A, B). These images should give a broader reflection of the actin populations and their dynamism during tube growth.
(b) A major reason why we use live imaging with actin reporters is that the distribution of actin around late endosomes and the tip compartment in general is very dynamic, so capturing cells at the right time point can be challenging from fixed samples. This problem is exacerbated by a technical limitation: For the actin cytoskeleton to be well preserved during fixation, embryos have to be manually dechorionated which limits the throughput of the experiment. We therefore found that analysing cells over time is more informative than analysing cells fixed at a given time point.
As the reviewer points out, using an overexpressed reporter can have drawbacks. With regard to the problem of not representing the endogenous distribution faithfully, this can be the case when making statements about the absolute distribution. However, what we are looking at here is not absolute quantities of actin but relative changes in the area of interest with respect to other, unaffected regions of the cells, and then comparing these between mutant conditions and the control. We do this by normalizing the signal to the levels seen in the subcellular tube, using it as an internal control that allows us to adjust for variation in expression levels.
There is on case where such a normalization could be problematic, and that is when comparing actin levels in cells expressing bitesize RNAi, because Bitesize is itself involved in organizing the actin cytoskeleton in the tube membrane (JayaNandanan et al., 2014). However, in this experiment, the analysis still shows that actin levels at late endosomes do not correlate with the tube misguidance phenotype.
With regard to potential physiological effects of an over-expressed construct, some of the commonly used actin reporters have subtle effects on actin physiology, whereas Utr-ABD has negligible or no effects on the actin cytoskeleton, and it also reproduces actin dynamics faithfully (Spracklen et al., 2014). It is therefore generally considered the most reliable tool for live imaging of actin in Drosophila.
We have adapted the text and commented on these issues and hoped we have achieved more clarity.
(c) We agree that when Vha or Wash are downregulated, actin levels are overall reduced in the growth cone of the cells, while this is not the case in other regions, for example at the base of the cell. Although we had not explicitly stated this (but now will), this is a further indication that the different actin populations in the growing tip interact with each other.
For the downregulation of Wash, this could potentially have been due to a direct effect of Wash on the apical and basal actin, but then we would have expected a similar result in other parts of the cell, including the cell body and the proximal part of the branch, but we do not see that. Even more importantly, the expression of Vha100-DN has the same effect and this cannot be easily explained by a direction action on actin. Together, these findings therefore indicate that depletion of actin around endosomes has a knock-on effect on the basal and apical actin cortex in the vicinity. We have included this reasoning in the paper now.
Another critical point in the model put forward by the authors is that late endosomes drive tube guidance. To test this point the authors use an elegant system to mislocalize Rab7 late endosomes.
However, the effects are not strong (1G), and only a proportion of branches show misguided tubes. Do the cases with a ventrally-guided tube in the experiment Rab7:YFP+/+ (Fig. 1G) have a CD4 endosome (with Rab7YFP) at the tip? This would help to explain the weak effect.
This is an excellent point, and it is indeed what we observe: all cells with ventrally guided tubes have a late endosome that is positive for the YRab7-nanobody-membrane complex at the tip of the cell (n=42), whereas only 2/3 of misguided tubes do (n = 12), and those always have the additional endosome at the tip of the misguide tube. As the reviewer suggests, this provides an obvious explanation for why these cells do not have a tube misguidance phenotype. We have added a representative image of this condition (Rab7::YFP+/+, ventrally-guided tube) in Figure 2 to illustrate the phenotype.
What is the cause that preventing proper endosome maturation and acidification leads to misguided tubes (rather than missing ones)?
A complete loss of late endosome activity would indeed result in the absence of the subcellular tube. However, we and others have shown that partial loss of function (as caused by RNAi) can have more subtle effects. For instance, fully blocking endocytosis using the shibire**ts line completely prevents proper tube extension (Mathew et al., 2020), but expression of a shibire RNAi still allows tube formation to proceed, albeit in a defective manner (Schottenfeld-Roames et al., 2014). Similarly, the misguidance phenotypes resulting from Vha downregulation likely reflect weaker loss of late endosome function. These perturbations would allow initial tube growth to proceed, but later on they would uncover this later function of the endocytic pathway in regulating tube guidance.
We believe that what we see as this weaker defect is an uncoupling of direction from growth per se. The cells still receive their growth-inducing signals from the FGF-receptor, and this leads to directed cell growth in the direction of the chemotactic signal. The normal trafficking of membrane material from the apical to the basal domain is also not disrupted. Thus, membrane keeps being added to both domains and both the tube and the basal domain continue to growth. However, the growing tube has been disconnected from its guiding structure at the tip of the cell (our speculation: because failed endosome maturation no longer allows proper actin coordination) and therefore follows a random path. We had not been sufficiently clear about this but have now hopefully remedied this in the text.
The authors indicate that downregulating Vha activity leads to defects in acidification, but late endosome-MVB normally form. It is intriguing to see extra CD4 vesicles (like in 1C or 6C).
Wouldn't we expect to see "normal" tip accumulation of CD4 vesicles only, and not extra ones? How relevant are these extra CD4 vesicles?
Wouldn't we expect to see "non functional" CD4 vesicles, unable to recruit actin and lead intracellular tube formation (i.e. no tube) rather than missguidances? (1D shows higher proportion of misguided tubes than no tubes)
Similarly, is Wash-RNAi producing extra CD4 vesicles (as observed in movie 5, fig 6E)?
We do not postulate that the late endosomes are morphologically normal – there are vesicles carrying the CD4 marker (which is only a membrane marker, not specific for endosomes), but the literature indicates that the endosomes do not undergo their normal maturations, and we would have no reason to claim otherwise. So we agree that the ones we see in the Vha-downregulated cells are not fully functional, and this is indeed confirmed by their inability to recruit actin.
With regard to the number of large CD4 vesicles at the tip, terminal cells can normally have from 1 to 3 in the growth cone, and the fact that the experimental cells we showed were at the upper range whereas the control at the lower end was pure chance. We have now quantified the number of vesicles in the abnormal conditions and see that there is no increase (Figure S5F).
Actin recruitment to late endosomes was already documented, where it plays a role in cargo trafficking.
The authors propose that Wash is recruited to late endosomes upon acidification where it would prime actin nucleation around the endosome. The authors indicate a decrease in Wash accumulation upon expression of Vha dominant negative. However, this decrease is not quantified. In addition, it is difficult to determine levels of a construct when this is overexpressed (UAS-Wash::GFP). It would be desirable to use antibodies against the endogenous protein (Wash in this case) to claim differences in accumulation in mutant conditions.
We have quantified the amount of Wash::GFP in CD4 vesicles. As mentioned, the vesicles are very dynamic, and so is their recruitment of Wash::GFP, and doing the analysis in the live cells is therefore more meaningful than extracting information from fixed samples, but we will also try to obtain the antibody for confirmation in fixed material. We appreciate that as discussed above for actin, results using overexpressed constructs have to be interpreted with care, but here again, we mitigate against this by assessing relative changes rather than absolute amounts and mitigate against misinterpretation by normalizing the signal to the one seen in the cytoplasm.
The results presented do not rule out a requirement of Wash in terminal branching which is not associated with the enrichment in the late endosomes. The genetic interaction observed with Shrub is also compatible with both proteins acting on terminal branching but in different/parallel mechanisms.
While the fact that downregulation of Vha has the same effect cannot be explained in this manner, we agree with the reviewer and will rephrase this section in the paper.
Laser ablation experiments
The laser ablation experiments are difficult to interpret.
First, it is unclear to me what the results exactly indicate. What does the recoil observed suggest? Does it fit with the expected tension exerted by a link of the actin cytoskeleton relayed by late endosomes?.
The observed recoil suggests that there was tension across the ablated area. The laser ablation experiments were one way to evaluate whether the actin cytoskeleton within the tip of the cell was continuous between the subcellular tube and the leading edge of the cell. Tension along this axis would support such a model. We assumed that if the actin cytoskeleton at the tip is continuous with both membrane compartments it was likely to be under tension, and our laser ablation experiments showed that is indeed the case. We have rewritten this section to make it clearer.
From the text and figure I don't understand how is the recoil calculated: retraction of the subcellular tube backwards? "enlargement" of the bleached area?
Briefly, we had used three measuring points: the backward displacement of (i) the subcellular tube and (ii) of the plasma membrane adjacent to the ablated area, which both retract towards the cell body, and we also measured (iii) the forward displacement of plasma membrane on the other side of the ablated area. We then calculated the average of these for each experiment.
However, we have now redone the evaluations of these experiments using PIV, an established method that is commonly used to calculate initial recoil after ablation and have explained this in the text.
Second, it is unclear to me what laser ablation actually ablates. Does it only affect actin? Or are also CD4-late endosomes and other tip structures affected?
The laser ablations with the conditions we use have in the past been shown to temporarily disrupt the actin cytoskeleton without otherwise damaging the cell (Rauzzi et al., 2015).
The ablations were done in cells that express the actin reporter Utr::GFP together with the membrane marker CD4::mIFP but we have no reason to believe that CD4 containing structures were damaged. For example, upon ablation, the CD4 vesicles in the ablated area are bleached, but in the recovery phase, we observe actin puncta in the positions where CD4 vesicles were originally located, suggesting that the vesicles themselves persist. Our interpretation of these observations is that the bleached CD4 vesicles do not recover their fluorescence (CD4::mIFP is an integral membrane protein and cannot simply be re-inserted within short periods), but they are still capable of recruiting actin. We have added a representative image of this to better describe the experiment (Fig. S4).
Third, is the recovery observed after ablation correlated with new actin recruitment around old or new late endosomes?
Actin rapidly reappears in the bleached area and the region that recoiled, where it is first seen in the basal cortex and filopodia. The tube re-extends towards the ablated area, and actin reassembles around the tube within seconds. During further recovery, actin reappears in puncta ahead of the tube and we assume that this is partly de novo assembly around the existing vesicles (Fig. S4A, B). At the same time, we also see new CD4 vesicles reaching the tip, so it is likely that both populations (old and new vesicles) mediate the recovery phase. We have added images of additional examples that illustrate these points.
Forth, I find the experiments in cells with secondary subcellular tubes very confusing and the explanations very speculative
The data on cuts in cells with tube duplications are indeed difficult to interpret, and because the emergence of secondary branches is unpredictable, it is not easy to obtain large numbers of observations. Figure S4 is another example of the response of these cells to the laser cut, and we will make clear that our interpretations are merely speculative.
Finally, and most importantly. I think that performing laser ablation experiments in mutant conditions that affect actin recruitment (VhaDN and Wash RNAi,....) would be very informative. One would expect to find a decrease in recoil. If this was the case, it would validate, on the one hand, that in control conditions there is a tension that depends (at least in part) on actin organization, and on the other hand it would show that when actin recruitment is affected tension decreases, supporting the "anchoring" model. I understand that laser ablation experiments are not easy to perform, but I think this would be a useful experiment.
To my understanding, as it stands, the laser ablation experiments "....support the notion that adequate cytoskeletal organization at the tip is required for tube guidance and stability" as the authors acknowledge, but they do not convincingly support their "anchoring" model
Laser cuts on cells that express Vha100-DN or wash-RNAi would be a nice addition that would take the work to the next level. But sadly, these are among the experiments that right now are impossible to carry out because of all the logistical and other problems resulting from the Covid pandemic, as explained in the cover letter.
**Other comments:**
- From the images presented, it is often difficult to figure out where the subcellular tube forms, the presence of vesicles, the cell morphologies,... and to determine the correlation between the CD4 vesicles and tube guidance.
This is the result of a frustrating technical limitation. In experiments in the past we have used markers for the outline of the cell, as we do here, too. Thus, where CD4 is expressed under the btl-gal4 driver it marks the entire outline of the cell against a completely negative background. Even for other markers, if expressed under btl-gal4, the outline of the cell is visible against the dark background. However, for endogenously marked proteins that are expressed ubiquitously, this is no longer true, and as we add more markers to follow different structures, we run out of fluorescent colours for everything we would like to highlight (and genetically, out of chromosomes to accommodate the necessary transgenic or endogenously modified constructs). We will provide tracings of the outlines of the cells to make the images clearer.
For instance, in Fig 1H and 1J, is there a "lateral" CD4 vesicle? Why it does not generate a missguided tube?
Yes, there are also CD4 vesicles closer to the proximal part of the cell. They are enriched at but not restricted to the tip of the cell. As we have shown previously (Mathew et al., 2020), they emerge along the subcellular tube, and most are transported towards the tip (also seen in Fig. 1A, for example). Why the remaining ones do not affect the guidance of the tube is unclear, but it is almost certain that the growth of the tip of the cells towards the chemotactic FGF signal plays a role: the basal membrane is constantly moving away from the tip of the tube at this location, but not at the sides further down the branch.
Fig 1I, are there 2 subcellular tubes? Can the authors mark them? I cannot really visualize them with the CD4 marker, they seem stalled or short or missing.
In Fig 1I, the tube is curled up inside of the cell, a phenotype often seen in larval terminal cells with excessive FGF signaling (for instance see Ukken et al., 2014). We added diagrams that explain the morphology of the tubes in this figure.
Fig 1L: what do the authors mean by "corrected" tube sprouts?
This is not well phrased, and we will also improve the figure to make the point clearer.
Panels 1K-M (now 1H-J) show snapshots from a movie of a cell that originally had only a misguided tube (at the top left) and is here in the process of forming its ‘correct’ tube growing in the ventral direction. In 1L (now 1I) this second tube is showing first signs of emerging, in 1M (now 1J) it is clearly visible. We have changed the wording in the figure and add an explanation in the legend, and we added a second example of this process in Figure S1.
It is difficult to identify the cell in Fig 2D-F
We added a dotted line in one of the channels showing the general morphology of the cell.
- Movie S3: I find it difficult to spot the association of CD4 and utrGFP that the authors point. Can the authors label in the movie the vesicles and the association?
We added pauses in the movie and arrows to the frames where actin is seen surrounding late endosomes.
- The results with the Rab7 downregulation and upregulation are not very clear.
Does the downregulation of Rab 7 (Rab7 DN construct) have any effect on tube guidance?
Does it decrease or eliminate actin association with CD4 vesicles in the embryo? The authors show that in the larvae expression of Rab7 DN leads to loss of actin enrichment in Rab7 vesicles. Does this have an effect on terminal branching?
Rab7DN is not visible in the embryo so we did not pursue further experiments in those stages and we previously showed that loss of Rab7 does not affect branching in larvae (Best and Leptin 2019). However, as the reviewer rightfully pointed out, expression of Rab7DN prevents actin nucleation at late endosomes in larval stages, so having the phenotypic consequence of this experiment would be informative and we are grateful for the observation. We had done the experiment, and we found no difference in the number of branches compared to controls. This suggests either that at larval stages actin recruitment at late endosomes is no longer required for branching or that there are redundant mechanisms that can balance the lack of actin nucleation. We favour the second model, because it has been shown that microtubules also play a role in tube branching and in coordinating the actin cytoskeleton (Araujo lab, 2021), so it is possible that actin nucleation can be bypassed. This is also consistent the fact that the phenotypes we describe are not all fully penetrant, again pointing to redundant mechanisms ensuring consistent directed growth.
We added the data regarding Rab7DN to the manuscript (Figure S2).
The Rab7 active construct produce effects at larval stages but not in the embryo. Is terminal cell branching in the larvae also dependent on late endosomes? Can the authors show "excess" of late endosomes in the larvae that lead to extra terminal branches? Even that the authors indicate that they cannot detect Rab7Q67L, can they find any effect at embryonic stages (e.g. presence and position of CD4 vesicles, other unrelated effects,...)?
Expression of Rab7CA in the embryo generates similar defects as nanobody-mediated mislocalisation of Rab7. We include below an example for the reviewer, but we did not feel comfortable including these data in the paper because some technical complications made them impossible to document and interpret with the certainty that we would wish. Most importantly, the YFP fusion protein is not detectable at embryonic stages, even with the most sensitive microscopes and detectors available to us. This means that we cannot correlate the observed phenotypes with the presence or absence of Rab7CA, which in our view makes them too weak for publication. At face value, these results suggest that Rab7CA begins to trigger branching during embryonic development, which eventually leads to the excess number of branches we see in the larva, but alas, we think this is too speculative to include in the paper.
- In some examples in the movies there seem to be a correlation between CD4 vesicles presence/positioning and basal lamellipodia/filopodia or actin enrichment, and also in -btl experiments. Have the authors explored this? They may want to comment on this in the discussion section.
That is a very pertinent point, and we should indeed have commented on it. If we assume the reviewer is looking at examples such as the one in Fig. 1I (currently S1C), then the explanation is the following. The terminal cells in the embryo often form transient side-branches, presumably in response to a low level FGF signals from the environment. In those cases, the basal actin cytoskeleton rearranges in the branching area to form the filopodia that lead the outgrowth of the branch, and what the reviewer observed is that this transient branch also forms the late endosome structure that we see in the main or proper growth cone. Thus, the guiding FGF-signal leads to a reorganisation of the entire actin cytoskeleton in the growth cone, and the formation of the actin-covered endosome is part of that process. We have included this in the discussion.
Reviewer #2 (Significance (Required)):
This work is relevant for the morphogenesis field and deals with the important issue of how the cytoskeleton regulates shape and cellular events. The work represents a deep analysis of a specific issue in the specialized field of tracheal development, but the results may be relevant for other types of cells forming subcellular tubes. Describing a function of trafficking vesicles (late endosome in this case) in cell morphogenesis (in addition to cargo trafficking) in an in vivo system is also relevant to advance in the cell biology field.
**Referees cross-commenting**
I agree with the comments of reviewer #1. I find relevant the points raised in "major comments number 2 and 4".
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
**Summary:**
The authors investigate the role of late endosomes in
the context of actin organization during cell morphogenesis. They use as experimental model the polarized terminal cells in the Drosophila tracheal system that forms a sub-cellular projection containing a tube. The authors show that disruption of the sub-cellular localization or maturation of late endosomes leads to increased proportion of terminal cells with mis-guided tubes. Their analysis indicated that endosomal F-actin recruitment is crucial for the directionality of the tube growth. The authors propose a model where, late endosomes control a coordinated crosstalk between endosomal and cortical actin pools to drive subcellular tube-guidance.
**Major comments:**
- The conclusion about how WASH functions in the tube-guidance, is not clearly shown and it should be better explained and documented. It is known that loss of function of the WASH leads to dysregulation of endosomal tubulation inducing enlarged endosomes, which in turn affects the endosome-to-plasma-membrane recycling of various cargos (including luminal cargos like Serp) (Gomez, et al., Mol. Biol. Cell, 2012; Dong et al, Nat. Comm. 2013). The authors should clarify if there is a defect in the integrity of endosomes located close to the cell tip in the btl>WASHIR knock down. In the cartoon panel C' (Figure 7), the endosomes in the cell tip are shown intact (Including their relative position to the tip) but no experimental data support this conclusion.
Given the fact that Wash contributes to proper late endosome morphology we do not necessarily expect the endosomes to look normal. We had not shown this in the diagram because our own data do not directly address this point, but the literature is of course clear enough about this, so we have modified our diagrams so that they better reflect the expected phenotypes and included a reference to the relevant literature.
We and others have shown the important role of late endosomes in plasma membrane and luminal cargo delivery, and as elaborated in the response to referee 2’s point 3, complete loss of endosomal function blocks these processes. Here, at reduced but not abolished function plasma membrane delivery is clearly still functional.
-The functional analysis of WASH was based on RNAi knock down. The authors express a single RNAi construct against WASH. The expression of this RNAi line gave a low penetrance phenotype. A well-known caveat of RNAi is off-targeting. Hence, phenotypic analysis needs to include a verification by a second independent RNAi construct or a rescue of the RNAi phenotype with an overexpressed cDNA of WASH. Ideally, the null wash mutant (Nagel et al. 2017) can be used to confirm the phenotype.
Analysing wash mutants would provide a welcome additional confirmation of the knockdown results, and it is true in general that poorly characterised RNAi lines can have off target effects. However, this is a well validated line: Nagel et al. (2017) showed that the same RNAi line that we used fully recapitulates the phenotype seen in wash mutants: In both cases, actin fails to localize to late endosomes, and this is what we also found in terminal cells.
Whereas we believe therefore that the experiment is not essential to support our conclusions, we agree it is desirable and have ordered these flies. However, progress is being hampered by import restrictions at the first author’s lab: the necessary paperwork for flies to be imported for his work is still under revision by officials. The experiment thus cannot be done at the moment.
The authors claim a role of the late endosomes in subcellular tube growth and guidance. But show no data on lumen formation to prove tube presence in the tracheal terminal cells of V100R755A, btl>WASHIR, shrb mutants or in GrabFP-Bint treated terminal cells. The interpretation and quantification of the phenotypic classes "miss-tube-guided" and "ventrally-tube-guided" are based on membrane markers and not on luminal markers. The presented data with the provided resolution does not prove if the mCD4-mIFP or PH-GFP markers define apical membrane protrusions/extensions or tubular structures. Therefore, the classifications of the tube-guidance phenotype and the quantification of "distance from tube to tip" may be suggestive. The authors need to provide additional confocal data of co.stainings of the endosomal compartments with luminal antigens (i.e. GASP or Serp or Verm).
We are very unsure as to what this would add and in what context it would be necessary. Membrane and actin markers have been widely used to follow the formation of the subcellular tube by all groups working in this field. There is ample documentation in the literature that the subcellular tube, as defined by luminal content (Serp, Verm, Gasp, CBP-GFP, ANF-GFP) is surrounded by apical plasma membrane which carries apical transmembrane proteins (Crb, Uif) and their associated apical cytoplasmic complexes (Par3, Par6, aPKC, pMoesin), and apical phospholipids which can be visualized by specific PIP-binding markers, e. g. The PLC-d PH-domain that binds to PIP2 (see, e.g., Kato et al., 2004; Oshima et al., 2006; Okenve-Ramos & Llimargas, 2014 (here they use both luminal and actin reporters); Ochoa-Espinosa et al., 2017; and from our lab: JayaNandanan et al., 2014; Mathew et al., 2020. Therefore, all labs in this field have used these markers interchangeably to visualize the subcellular tube and we are not aware of a single case where luminal shape and apical membrane shape were not exactly congruent.
We have in fact used luminal markers in some experiments here, but we believe there is no reason to assume that luminal markers would have a different distribution compared to membrane, apical or actin reporters in any the experiments described here. Finally, the focus of the paper is on the behaviour of the early out-growing membrane rather than the mature tube, and on how membrane is remodelled in this process by modifications in the actin cytoskeleton. Including confirmation of the presence of luminal material would not add to the paper.
page 8 line 248, the authors interpret that reducing the dose of Shrb by half strongly enhances the wash-RNAi phenotype and suggest that WASH and Shrb act in the same pathway. Shrub is a subunit of the ESCRT-III complex involved in inward membrane budding of endosomes and WASH functions in outward endosomal membrane budding.
The Shrb and WASH form discrete molecular complexes in endosomes. The authors should consider that Shrb and WASH may well act in parallel to control directional tube growth.
This is a good point and we will rephrase our conclusions from this experiment.
The authors use nanobody-based GFP trap construct to investigate the effect of Rab7YFP localization. This is an excellent way to provide novel information for protein miss-localization in vivo. Using this method the authors concluded that ... "the correct distribution of late endosomes is required for proper tube guidance" (page 5, lines 157-158). The authors obviously consider that GrabFP-B-Int construct affected the distribution of late endosomes. However, this is unclear and additional control experiments are needed to support the author's claims. For instance, did expression of GrabFP-B-Int, target the Rab7-YFP protein or the Rab7-associated endosomes? With the presented data, it is not clear if the Rab7-YFP positive vesicles are endosomes? or aggregates formed by the trapped Rab7-YFP protein? Co-stainings using GFP in Rab7-YFP terminal cells with another endosomal markers i.e. Avl, or hrs, should be provided. It is also not clear if endocytosis of apical/basal membrane or luminal cargos was affected in GrabFP-B-Int treated terminal cells. The loss of endocytic components has been associated with defects in subcellular tube shape and morphology (Schottenfeld-Roames et al, Cur Biol. 2014). The authors should clarify these issues.
The nanobody would of course bind both to free Rab7::YFP (if there is any available) and to endosome-associated Rab7::YFP. However, in addition to Rab7::YFP we also assayed the distribution of CD4::mIFP, a membrane-associated protein that is seen at very low levels in all membranes (Mathew et al., 2020), but highly enriched in cytoplasmic vesicles, which we showed by co-expressed markers to correspond to endosomes (Mathew et al., 2020). If the nanobody sequestered free Rab7::YFP, we would expect little overlap between Rab7::YFP and CD4::mIFP puncta. Instead, we see that the large Rab7::YFP/nanobody puncta have membrane associated with them (63% of vesicles are triple positive, vs 8% of Rab7::YFP-GrabFP vesicles) indicating that they are not merely Rab7 aggregates. We will include a quantification of the degree of overlap between these components.
Regarding the question of whether endocytosis is affected, we believe this is unlikely, or if it is at all, only to a minimal extent, since growth of the outer membrane, which crucially depends on endocytosis, continues in these cells. We have added a comment to this effect in the text. The cells look very different from cells in which endocytosis has been inhibited.
In the legends of Figure 7 (C'), the authors stated that.... "lack of actin regulators at the basal cortex prevents the connection of the actin meshwork at the tip to the basal plasma membrane".... by depicting the singed mutant phenotype. singed mutant analysis is not shown in the manuscript.
Singed/Fascin has previously been shown to be required for actin organization in fillopodia (Okenve-Ramos & Llimargas, 2014). We have now included new data that show that cells expressing singed RNAi also have reducedamounts of actin at late endosomes, and that reduced actin correlates strongly with tube misguidance. This shows that an actin bundling protein that has previously been shown to be needed for actin bundles in filopodia again affects actin around endosomes, providing another illustration that these compartments interact with each other.
Our quantifications on actin around late endosomes show that interfering with endosome maturation, actin nucleation via Wash and basal/filopodial actin all lead to loss of actin around endosomes, and the misguidance phenotype correlates with actin loss (Figure 6J). By contrast, disruption of the apical actin cortex does not affect endosomal actin but does lead to misguidance. This establishes a hierarchy of actin organisation in the tip of the cell: basal actin affects endosomal actin, loss endosomal actin affects both apical and basal actin, but apical actin does not feed back on endosomal. All three pools are nevertheless required for tube guidance.
The authors consider the late endosomes nucleate actin ahead of the tube (i.e. page3, line 87-88, page 9, line 285). This is not very convincing from the presented data. The authors should provide some quantitative data showing that lack of WASH (and endosomal F-actin network) effects the apical and basal F-actin pools in the tip of the cell.
If we understand the reviewer correctly, there are two comments included in this point: (i) whether actin is nucleated at late endosomes, and (ii), whether reducing endosomal F-actin affects apical-basal actin pools in the tip of the cell.
(i) As stated above in the response to reviewer #2, we have added quantitative data illustrating actin recruitment at late endosomes with phalloidin stainings. Actin association with endosomes is also confirmed by the Rab7 stainings in larval terminal cells in Fig. 3G-H that show actin puncta associated with endosomes.
(ii) Again, as mentioned in the response to reviewer #2, we do think that all actin pools in the growth cone are affected. We are glad that the reviewers encouraged us to make this more explicit and will now discuss more clearlyhow endosomal F-actin could affect apical and basal F-actin pools.
**Minor concerns:**
- The authors concluded (page 9, line 285) that "endosomes serve as actin nucleating centres that propagate forces within the cell by physically linking different subcellular compartments".
We agree with the reviewer, this is a good way of phrasing it, and we will rewrite this conclusion accordingly.
The authors should depict in the panels the Ventral/Dorsal axis.
All images are positioned in the same orientation, but we will ensure that the D/V axis orientation is stated in the manuscript.
Numerous omissions need to be corrected. Labeling is missing in the panels J-M' (Figure 1). The statistical significance and the p values levels are not indicated in Figure 2 (G). The panel figure 5 (D) is miss-labelled. The panels C-C' in f igure 7 are not very informative. They do not reflect the general model of the study. How the prevention of actin nucleation at late endosomes, or apical or basal cortex affects tube directionality is not graphically shown.
We thank the reviewer for noticing these omissions, we will fix them for resubmission. Having added more discussion about the general organization of actin at the tip of the cell, we think the relevance of panels 7C is justified.
In the section "Crosstalk between cytoskeletal compartments" (Lines 359- 400, discussion) the argument about the involvement of microtubules in tube-guidance is a likely scenario. But I found this argument over-extended. WASH interacts with tubulin Derivery et al. Dev Cell (2009) and WASH activity balances the endosomal and cortical F-actin networks during epithelial tube maturation in multicellular tracheal tubes (Tsarouhas et al., Nat. Comm 2019). These results should be considered in the discussion section.
We will incorporate these references to the discussion, they will for sure enrich it.
Reviewer #1 (Significance (Required)):
The important role of actin cytoskeleton in the initiation of endocytosis is well established. Actin structures in the plasma membrane are dynamically organized to assist the remodeling of the cell surface and to facilitate the inward movement of vesicles. Similarly actin networks in endosomes are critical for endosomal fusion and fission. In this work, the authors identified an opposing but interesting scenario. They propose a role for the late endocytic pathway in organizing actin networks for proper cell morphogenesis and point out an intracellular crosstalk and coordination between distinct cytoskeletal pools within a cell.
Although the mechanism about how the separate F-actin pools communicate is not shown, the paper is interesting and shows an original contribution in the area of cell morphogenesis. In addition it represents a conceptual advance as it proposes a mechanism through which actin cytoskeleton is coordinated to regulate tube morphogenesis. The proposed mechanism may be relevant for tracheal terminal cells, but could represent a general mechanism in the field of cell biology. The methodology is appropriate and the text flow is well organized. However, as explained, there are few inconsistencies in the manuscript. I believe the above additions would strengthen the conclusion of the paper.
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Referee #2
Evidence, reproducibility and clarity
Summary
Rios-Barrera and Leptin investigate the formation and guidance of the subcellular tube that forms in the terminal cell of the dorsal branches of the Drosophila tracheal system. In previous work the authors documented the presence of late endosomes at the tip of the growing terminal cell, ahead of the forming subcellular tube, which are involved in membrane recycling {Mathew, 2020 #1407}. In this present work they analyze the organization of the actin cytoskeleton in the tip terminal cell, in relation with the late endosomes, and assess the guidance of the subcellular tube. They find that the presence and localization of late endosomes play a role in tube guidance. They also find that late endosomes recruit actin around them, mediated by the activity of the actin polymerization regulator Wash, which is recruited to maturing late endosomes. When Wash activity is decreased, actin around late endosomes is decreased and tube guidance is compromised. Based on this observation, laser ablation experiments of actin ahead of the tube and actin staining at the tip of the terminal cell, the authors propose an exciting model: late endosomes recruit actin, which connects the actin pool of the basal membrane and the actin pool of the apical (subcellular tube) membrane thereby directing tube growth and guidance. The manuscript is well-written and well-presented, the images and movies are of high quality and the experimental data, which is technically challenging, is very good and sufficiently replicated.
Major comments:
- A critical point in the model that the authors put forward (which is also contained in the title and abstract) is that actin organized at late endosomes anchors apical and basal actin cortices. However, there is no clear and conclusive evidence for this. Clear evidence in this direction should be provided to propose it as a mechanism (as it is in the text, particularly in the first sentences of the discussion) and imply it in the title.
The authors show endogenous actin around late endosomes and actin fibers at the tip of the terminal branch. However, at the level of resolution presented (Fig 3A,B), it is not possible to determine whether the different actin populations are actually "anchored". I suggest to present stronger data supporting this important conclusion.
In the same direction, it would be critical to show that this anchoring of actin fibers is disturbed when actin enrichment at the late endosome is perturbed (see also point 5). Actually, the authors show that when Vha or Wash activity are downregulated actin accumulation around the CD4 vesicles decrease. However, this experiment has a few inconveniences. First, it is difficult to determine levels of a construct that is overexpressed (UAS-utr::GFP). Could the authors use phalloidin or an actin antibody to confirm the result? Second, I find the result difficult to interpret. In the images provided I see a general decrease of actin (UtrGFP) at the tip, not only around the CD4 vesicles (Fig 6D,F) . Are these mutant conditions also affecting the rest of actin pools? If this is the case, can the authors attribute the defects exclusively to the abnormal recruitment of actin to the late endosomes? Most importantly, the authors should analyze the pattern of actin distribution (labelling endogenous actin) and determine a possible loss of "anchoring" of fibers when late endosome maturation is perturbed.
- Another critical point in the model put forward by the authors is that late endosomes drive tube guidance. To test this point the authors use an elegant system to mislocalize Rab7 late endosomes. However, the effects are not strong (1G), and only a proportion of branches show misguided tubes. Do the cases with a ventrally-guided tube in the experiment Rab7:YFP+/+ (Fig. 1G) have a CD4 endosome (with Rab7YFP) at the tip? This would help to explain the weak effect.
- What is the cause that preventing proper endosome maturation and acidification leads to misguided tubes (rather than missing ones)? The authors indicate that downregulating Vha activity leads to defects in acidification, but late endosome-MVB normally form. It is intriguing to see extra CD4 vesicles (like in 1C or 6C). Wouldn't we expect to see "normal" tip accumulation of CD4 vesicles only, and not extra ones? How relevant are these extra CD4 vesicles? Wouldn't we expect to see "non functional" CD4 vesicles, unable to recruit actin and lead intracellular tube formation (i.e. no tube) rather than missguidances? (1D shows higher proportion of misguided tubes than no tubes) Similarly, is Wash-RNAi producing extra CD4 vesicles (as observed in movie 5, fig 6E)?
- Actin recruitment to late endosomes was already documented, where it plays a role in cargo trafficking. The authors propose that Wash is recruited to late endosomes upon acidification where it would prime actin nucleation around the endosome. The authors indicate a decrease in Wash accumulation upon expression of Vha dominant negative. However, this decrease is not quantified. In addition, it is difficult to determine levels of a construct when this is overexpressed (UAS-Wash::GFP). It would be desirable to use antibodies against the endogenous protein (Wash in this case) to claim differences in accumulation in mutant conditions.
The results presented do not rule out a requirement of Wash in terminal branching which is not associated with the enrichment in the late endosomes. The genetic interaction observed with Shrub is also compatible with both proteins acting on terminal branching but in different/parallel mechanisms.
- Laser ablation experiments The laser ablation experiments are difficult to interpret. First, it is unclear to me what the results exactly indicate. What does the recoil observed suggest? Does it fit with the expected tension exerted by a link of the actin cytoskeleton relayed by late endosomes?. From the text and figure I don't understand how is the recoil calculated: retraction of the subcellular tube backwards? "enlargement" of the bleached area? Second, it is unclear to me what laser ablation actually ablates. Does it only affect actin? Or are also CD4-late endosomes and other tip structures affected? Third, is the recovery observed after ablation correlated with new actin recruitment around old or new late endosomes? Forth, I find the experiments in cells with secondary subcellular tubes very confusing and the explanations very speculative Finally, and most importantly. I think that performing laser ablation experiments in mutant conditions that affect actin recruitment (VhaDN and Wash RNAi,....) would be very informative. One would expect to find a decrease in recoil. If this was the case, it would validate, on the one hand, that in control conditions there is a tension that depends (at least in part) on actin organization, and on the other hand it would show that when actin recruitment is affected tension decreases, supporting the "anchoring" model. I understand that laser ablation experiments are not easy to perform, but I think this would be a useful experiment. To my understanding, as it stands, the laser ablation experiments "....support the notion that adequate cytoskeletal organization at the tip is required for tube guidance and stability" as the authors acknowledge, but they do not convincingly support their "anchoring" model
Other comments:
- From the images presented, it is often difficult to figure out where the subcellular tube forms, the presence of vesicles, the cell morphologies,... and to determine the correlation between the CD4 vesicles and tube guidance. For instance, in Fig 1H and 1J, is there a "lateral" CD4 vesicle? Why it does not generate a missguided tube? Fig 1I, are there 2 subcellular tubes? Can the authors mark them? I cannot really visualize them with the CD4 marker, they seem stalled or short or missing. Fig 1L: what do the authors mean by "corrected" tube sprouts? It is difficult to identify the cell in Fig 2D-F
- Movie S3: I find it difficult to spot the association of CD4 and utrGFP that the authors point. Can the authors label in the movie the vesicles and the association?
- The results with the Rab7 downregulation and upregulation are not very clear. Does the downregulation of Rab 7 (Rab7 DN construct) have any effect on tube guidance? Does it decrease or eliminate actin association with CD4 vesicles in the embryo? The authors show that in the larvae expression of Rab7 DN leads to loss of actin enrichment in Rab7 vesicles. Does this have an effect on terminal branching? The Rab7 active construct produce effects at larval stages but not in the embryo. Is terminal cell branching in the larvae also dependent on late endosomes? Can the authors show "excess" of late endosomes in the larvae that lead to extra terminal branches? Even that the authors indicate that they cannot detect Rab7Q67L, can they find any effect at embryonic stages (e.g. presence and position of CD4 vesicles, other unrelated effects,...)?
- In some examples in the movies there seem to be a correlation between CD4 vesicles presence/positioning and basal lamellipodia/filopodia or actin enrichment, and also in -btl experiments. Have the authors explored this? They may want to comment on this in the discussion section.
Significance
This work is relevant for the morphogenesis field and deals with the important issue of how the cytoskeleton regulates shape and cellular events. The work represents a deep analysis of a specific issue in the specialized field of tracheal development, but the results may be relevant for other types of cells forming subcellular tubes. Describing a function of trafficking vesicles (late endosome in this case) in cell morphogenesis (in addition to cargo trafficking) in an in vivo system is also relevant to advance in the cell biology field.
Referees cross-commenting
I agree with the comments of reviewer #3. I find relevant the points raised in "major comments number 2 and 4".
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Referee #1
Evidence, reproducibility and clarity
Summary:
The authors investigate the role of late endosomes in the context of actin organization during cell morphogenesis. They use as experimental model the polarized terminal cells in the Drosophila tracheal system that forms a sub-cellular projection containing a tube. The authors show that disruption of the sub-cellular localization or maturation of late endosomes leads to increased proportion of terminal cells with mis-guided tubes. Their analysis indicated that endosomal F-actin recruitment is crucial for the directionality of the tube growth. The authors propose a model where, late endosomes control a coordinated crosstalk between endosomal and cortical actin pools to drive subcellular tube-guidance.
Major comments:
- The conclusion about how WASH functions in the tube-guidance, is not clearly shown and it should be better explained and documented. It is known that loss of function of the WASH leads to dysregulation of endosomal tubulation inducing enlarged endosomes, which in turn affects the endosome-to-plasma-membrane recycling of various cargos (including luminal cargos like Serp) (Gomez, et al., Mol. Biol. Cell, 2012; Dong et al, Nat. Comm. 2013). The authors should clarify if there is a defect in the integrity of endosomes located close to the cell tip in the btl>WASHIR knock down. In the cartoon panel C' (Figure 7), the endosomes in the cell tip are shown intact (Including their relative position to the tip) but no experimental data support this conclusion.
-The functional analysis of WASH was based on RNAi knock down. The authors express a single RNAi construct against WASH. The expression of this RNAi line gave a low penetrance phenotype. A well-known caveat of RNAi is off-targeting. Hence, phenotypic analysis needs to include a verification by a second independent RNAi construct or a rescue of the RNAi phenotype with an overexpressed cDNA of WASH. Ideally, the null wash mutant (Nagel et al. 2017) can be used to confirm the phenotype.
- The authors claim a role of the late endosomes in subcellular tube growth and guidance. But show no data on lumen formation to prove tube presence in the tracheal terminal cells of V100R755A, btl>WASHIR, shrb mutants or in GrabFP-Bint treated terminal cells. The interpretation and quantification of the phenotypic classes "miss-tube-guided" and "ventrally-tube-guided" are based on membrane markers and not on luminal markers. The presented data with the provided resolution does not prove if the mCD4-mIFP or PH-GFP markers define apical membrane protrusions/extensions or tubular structures. Therefore, the classifications of the tube-guidance phenotype and the quantification of "distance from tube to tip" may be suggestive. The authors need to provide additional confocal data of co.stainings of the endosomal compartments with luminal antigens (i.e. GASP or Serp or Verm).
- page 8 line 248, the authors interpret that reducing the dose of Shrb by half strongly enhances the wash-RNAi phenotype and suggest that WASH and Shrb act in the same pathway. Shrub is a subunit of the ESCRT-III complex involved in inward membrane budding of endosomes and WASH functions in outward endosomal membrane budding. The Shrb and WASH form discrete molecular complexes in endosomes. The authors should consider that Shrb and WASH may well act in parallel to control directional tube growth.
- The authors use nanobody-based GFP trap construct to investigate the effect of Rab7YFP localization. This is an excellent way to provide novel information for protein miss-localization in vivo. Using this method the authors concluded that ... "the correct distribution of late endosomes is required for proper tube guidance" (page 5, lines 157-158). The authors obviously consider that GrabFP-B-Int construct affected the distribution of late endosomes. However, this is unclear and additional control experiments are needed to support the author's claims. For instance, did expression of GrabFP-B-Int, target the Rab7-YFP protein or the Rab7-associated endosomes? With the presented data, it is not clear if the Rab7-YFP positive vesicles are endosomes? or aggregates formed by the trapped Rab7-YFP protein? Co-stainings using GFP in Rab7-YFP terminal cells with another endosomal markers i.e. Avl, or hrs, should be provided. It is also not clear if endocytosis of apical/basal membrane or luminal cargos was affected in GrabFP-B-Int treated terminal cells. The loss of endocytic components has been associated with defects in subcellular tube shape and morphology (Schottenfeld-Roames et al, Cur Biol. 2014). The authors should clarify these issues.
- In the legends of Figure 7 (C'), the authors stated that.... "lack of actin regulators at the basal cortex prevents the connection of the actin meshwork at the tip to the basal plasma membrane".... by depicting the singed mutant phenotype. singed mutant analysis is not shown in the manuscript.
- The authors consider the late endosomes nucleate actin ahead of the tube (i.e. page3, line 87-88, page 9, line 285). This is not very convincing from the presented data. The authors should provide some quantitative data showing that lack of WASH (and endosomal F-actin network) effects the apical and basal F-actin pools in the tip of the cell.
Minor concerns:
- The authors concluded (page 9, line 285) that "endosomes serve as actin nucleating centres that propagate forces within the cell by physically linking different subcellular compartments". The authors may want to consider that endosomes can serve as platforms to assemble important actin polymerization regulators and/or signals in the tip of the terminal cell to instruct tube directionality.
- The authors should depict in the panels the Ventral/Dorsal axis.
- Numerous omissions need to be corrected. Labeling is missing in the panels J-M' (Figure 1). The statistical significance and the p values levels are not indicated in Figure 2 (G). The panel figure 5 (D) is miss-labelled. The panels C-C' in figure 7 are not very informative. They do not reflect the general model of the study. How the prevention of actin nucleation at late endosomes, or apical or basal cortex affects tube directionality is not graphically shown.
- In the section "Crosstalk between cytoskeletal compartments" (Lines 359- 400, discussion) the argument about the involvement of microtubules in tube-guidance is a likely scenario. But I found this argument over-extended. WASH interacts with tubulin Derivery et al. Dev Cell (2009) and WASH activity balances the endosomal and cortical F-actin networks during epithelial tube maturation in multicellular tracheal tubes (Tsarouhas et al., Nat. Comm 2019). These results should be considered in the discussion section.
Significance
The important role of actin cytoskeleton in the initiation of endocytosis is well established. Actin structures in the plasma membrane are dynamically organized to assist the remodeling of the cell surface and to facilitate the inward movement of vesicles. Similarly actin networks in endosomes are critical for endosomal fusion and fission. In this work, the authors identified an opposing but interesting scenario. They propose a role for the late endocytic pathway in organizing actin networks for proper cell morphogenesis and point out an intracellular crosstalk and coordination between distinct cytoskeletal pools within a cell.
Although the mechanism about how the separate F-actin pools communicate is not shown, the paper is interesting and shows an original contribution in the area of cell morphogenesis. In addition it represents a conceptual advance as it proposes a mechanism through which actin cytoskeleton is coordinated to regulate tube morphogenesis. The proposed mechanism may be relevant for tracheal terminal cells, but could represent a general mechanism in the field of cell biology. The methodology is appropriate and the text flow is well organized. However, as explained, there are few inconsistencies in the manuscript. I believe the above additions would strengthen the conclusion of the paper.
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity (Required)): Very high evidence and clarity. Excellent scientific rigor. The findings are important and reported clearly. The experiments are conducted in a rigorous way by numerous participating laboratories. Reviewer #1 (Significance (Required)): Very high significance, both from a molecular biology and clinical standpoints. This is an important manuscript that challenges the findings and conclusions of a prior high-profile paper in Science by Ma et al 2016, claiming that LAG3 is a receptor for aggregation-prone species of alpha-synuclein and that deletion of LAG3 results in reduced cell to cell propagation of alpha-synuclein aggregates. The experiments in this paper are numerous and employ a variety of techniques. The overall conclusions are that LAG3 is not expressed by the relevant neurons and that LAG3 is not a receptor for alpha-synuclein fibrils (of different sizes). Therefore, the authors conclude that LAG3 is unlikely to play a role in the spread of alpha-synuclein pathology in Parkinson's disease and related disorders. There are, however, some weaknesses. For example, the Introduction contains passages that are not written in a stringent way: 1. "Histologically, PD is characterized by α-synuclein aggregates known as Lewy Bodies in neurons of the substantia nigra," That is not a good description of PD neuropathology. Lewy pathology is present in numerous areas of the CNS and PNS, and is not restricted to the substantia nigra.
We have added a more detailed account:
“Histologically, PD is characterized by α-synuclein inclusions known as Lewy Bodies whose accumulation is associated with neurodegeneration (Dickson, 2012; Mullin and Schapira, 2015; Corbillé et al., 2016). These inclusions affect the Substantia nigra and other mesencephalic regions as well as, in some cases, the amygdala and neocortex (Dickson, 2018).”
- "Growing evidence suggests that α-synuclein fibrils spread from cell to cell". While alpha-synuclein pathology can spread from cell to cell, it is not known if the fibrils are the species (alone or combined with other conformers) that cause the spreading of the pathology in a seeding fashion, or if smaller alpha-synuclein assemblies play that role.
We have reformulated the sentence to credit the fact that we do not know which synuclein species is the one that is transmitted:
“Growing evidence suggests that α-synuclein aggregates spread from cell to cell (Volpicelli-Daley et al., 2011; Volpicelli-Daley, Luk and Lee, 2014)… “
- "...by a "prionoid" process of templated conversion (Aguzzi, 2009; Aguzzi and Lakkaraju, 2016; Jucker and Walker, 2018; Kara, Marks and Aguzzi, 2018; Scheckel and Aguzzi, 2018; Uemura et al., 2020)." This sentence gives the impression that the corresponding author has led the field when it comes to alpha-synuclein's prionid properties. That is not really the case, and it would be appropriate to cite the literature in a more scholarly fashion that reflects how this part of the alpha-synuclein research field developed.
I cannot disagree, and in fact I suspect that the present paper may be my second and possibly last experimental contribution to the synuclein field! However, I do claim intellectual parenthood of the prionoid (not “prionid”) concept, which I first expounded in a 2009 Nature paper. Anyway, we now provide a more balanced citation:
“…by a “prionoid” process of templated conversion (Aguzzi, 2009; Jucker and Walker, 2018; Kara, Marks and Aguzzi, 2018; Henderson, Trojanowski and Lee, 2019; Karpowicz, Trojanowski and Lee, 2019; Uemura et al., 2020; Kara et al., 2021).“
- "Interrupting transmission of a-synuclein may slow down or abrogate the disease course." This is a bold statement and far from certain. While one might propose that this is the case, it is still just a hypothesis and the Introduction should reflect that.
We have rewritten the sentence in a more subdued manner:
“It is thought that interrupting transmission of a-synuclein may slow down or abrogate the disease course.”
**Referee Cross-commenting** I concur with reviewers 2 and 3, and the new comment from reviewer 2. This paper should be published as soon as possible.
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Reviewer #2 (Evidence, reproducibility and clarity (Required)): This study conclusively shows that LAG3 is not the receptor for a-synuclein that underlies the spread of synucleinopathic damage in various PD-related conditions. The paper is done extremely carefully and comprehensively. My only suggestion is to indicate the significance level in Figure 5a, as it may turn out that LAG3 is actually protective.
We have added the significance level in Fig. 5A, in the legend: “The survivals of ASYNA53T LAG3-/-, LAG3+/- and LAG3+/+ mice were similar (Mantel-Cox log-rank test, p-value = 0.165).”
Reviewer #2 (Significance (Required)): This study is of extremely high significance - we need mechanisms to deal with spectacular results in the literature that should not have been published because they are were uncompelling to begin with, but were published for various sociological/political reasons. Science won't progress if we don't find correction mechanisms for wrong conclusions. **Referee Cross-commenting** I agree with reviewers 1 and 3, especially with the suggestions made by reviewer 1, which should be instituted. I think we all concur that the paper should be published without new experiments. I believe testing a-synuclein propagation in vivo in LAG3 KO mice would be useful, but given the complete lack of replication of LAG3 expression in brain and of a-synuclein binding to LAG3, this is not necessary.
We considered running experiments in addition to those performed in vivo in ASYNA53T transgenic mice (including LAG3 KO) and ex vivo in organotypic slices, the latter using pre-formed fibrils. However, the outcome of these experiments, along with the absence of LAG3 expression in neurons and its unclear binding, convinced us that the usage of further animals and reagents would be unwarranted.
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Reviewer #3 (Evidence, reproducibility and clarity (Required)): It was proposed that LAG3 is important in the treatment of PD and related disorders, because it functions as a receptor of pathogenic α-synuclein and the treatment with anti-LAG3 antibodies attenuated the spread of pathological α-synuclein and drastically lowered the aggregation in vitro (Mao et al, Science 2016). In this study, authors characterized 8 antibodies to LAG3 and investigated the presence of LAG3 in cultured cell lines, NSC-derived neural cultures, or organ homogenates for the presence of human or murine LAG3. But it was not detected in any of the neuronal samples tested. In addition, single cell (sc) RNAseq yielded only minimal counts for the LAG3 transcript in neurons, astrocytes, and mixed glial cells, and single-nucleus (sn) RNAseq human brain dataset for LAG3 expression across different cell types confirmed no LAG3 signals for any of 34 identified cell clusters, including 13 clusters of excitatory and 11 subtypes of inhibitory neurons, oligodendrocytes, oligodendrocyte precursor cells, microglia, astrocytes, and endothelial cells. Authors also analyzed the binding of LAG3 with α-synuclein in mouse and human model systems, and concluded that the affinity of LAG3 for α-synuclein fibrils, if any, is micromolar or less. Furthermore, authors studied the propagation of pre-formed fibrils (PFFs) of α-synuclein in neural stem cell (NSC)-derived neural cultures in the presence or absence of LAG3, and the impact of LAG3 on survival in ASYNA53T transgenic mice expressing wild-type LAG3 as well as hemizygous or homozygous deletions thereof. However, they were unable to see any significant role for LAG3 in these in vitro and in vivo models of α-synucleinopathies. In this connection, the reviewer would like to ask one question: Have you conducted any experiments of the propagation of PFFs of α-synuclein in LAG3-KO mice ? If they did, what were the results ?
We did consider the possibility of replicating the experiments using PFFs in LAG3 KO mice. However, as stated above, we felt that our experiments – including the survival study in vivo in ASYNA53T transgenic mice – were unambiguous. After critical consideration, we remained unconvinced that this additional experiment would change the weight of our evidence in a substantial manner that would justify the inoculation of other animals and the utilisation of more resources.
**Minor point** In Page 10, I think it's a typo: ASYYN mice must be ASYN mice.
Thank you for pointing this out. We corrected it.
Reviewer #3 (Significance (Required)): These negative findings about the LAG in α-synucleinopathies shown in this manuscript do not provide any new insight into the mechanisms of α-synuclein propagation. However, it is clear that LAG3 is not expressed in neuronal cells and the binding of LAG3 to α-synuclein fibrils appears limited. Overexpression of LAG3 in cultured human neural cells did not cause any worsening of α-synuclein pathology ex vivo. The overall survival of A53T α- synuclein transgenic mice was unaffected by LAG3 depletion and the seeded induction of α-synuclein lesions in hippocampal slice cultures was unaffected by LAG3 knockout. These data shown in this manuscript are convincing and the information is very important in terms of correcting the direction of disease treatment and research. **Referee Cross-commenting** I agree with reviewers 1 and 2. This paper should be published as soon as possible.
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Referee #3
Evidence, reproducibility and clarity
It was proposed that LAG3 is important in the treatment of PD and related disorders, because it functions as a receptor of pathogenic α-synuclein and the treatment with anti-LAG3 antibodies attenuated the spread of pathological α-synuclein and drastically lowered the aggregation in vitro (Mao et al, Science 2016).
In this study, authors characterized 8 antibodies to LAG3 and investigated the presence of LAG3 in cultured cell lines, NSC-derived neural cultures, or organ homogenates for the presence of human or murine LAG3. But it was not detected in any of the neuronal samples tested. In addition, single cell (sc) RNAseq yielded only minimal counts for the LAG3 transcript in neurons, astrocytes, and mixed glial cells, and single-nucleus (sn) RNAseq human brain dataset for LAG3 expression across different cell types confirmed no LAG3 signals for any of 34 identified cell clusters, including 13 clusters of excitatory and 11 subtypes of inhibitory neurons, oligodendrocytes, oligodendrocyte precursor cells, microglia, astrocytes, and endothelial cells.
Authors also analyzed the binding of LAG3 with α-synuclein in mouse and human model systems, and concluded that the affinity of LAG3 for α-synuclein fibrils, if any, is micromolar or less.
Furthermore, authors studied the propagation of pre-formed fibrils (PFFs) of α-synuclein in neural stem cell (NSC)-derived neural cultures in the presence or absence of LAG3, and the impact of LAG3 on survival in ASYNA53T transgenic mice expressing wild-type LAG3 as well as hemizygous or homozygous deletions thereof. However, they were unable to see any significant role for LAG3 in these in vitro and in vivo models of α-synucleinopathies.
In this connection, the reviewer would like to ask one question: Have you conducted any experiments of the propagation of PFFs of α-synuclein in LAG3-KO mice ? If they did, what were the results ?
Minor point
In Page 10, I think it's a typo: ASYYN mice must be ASYN mice.
Significance
These negative findings about the LAG in α-synucleinopathies shown in this manuscript do not provide any new insight into the mechanisms of α-synuclein propagation. However, it is clear that LAG3 is not expressed in neuronal cells and the binding of LAG3 to α-synuclein fibrils appears limited. Overexpression of LAG3 in cultured human neural cells did not cause any worsening of α-synuclein pathology ex vivo. The overall survival of A53T α- synuclein transgenic mice was unaffected by LAG3 depletion and the seeded induction of α-synuclein lesions in hippocampal slice cultures was unaffected by LAG3 knockout. These data shown in this manuscript are convincing and the information is very important in terms of correcting the direction of disease treatment and research.
Referee Cross-commenting
I agree with reviewers 1 and 2. This paper should be published as soon as possible.
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Referee #2
Evidence, reproducibility and clarity
This study conclusively shows that LAG3 is not the receptor for a-synuclein that underlies the spread of synucleinopathic damage in various PD-related conditions. The paper is done extremely carefully and comprehensively. My only suggestion is to indicate the significance level in Figure 5a, as it may turn out that LAG3 is actually protective.
Significance
This study is of extremely high significance - we need mechanisms to deal with spectacular results in the literature that should not have been published because they are were uncompelling to begin with, but were published for various sociological/political reasons. Science won't progress if we don't find correction mechanisms for wrong conclusions.
Referee Cross-commenting
I agree with reviewers 1 and 3, especially with the suggestions made by reviewer 1, which should be instituted. I think we all concur that the paper should be published without new experiments. I believe testing a-synuclein propagation in vivo in LAG3 KO mice would be useful, but given the complete lack of replication of LAG3 expression in brain and of a-synuclein binding to LAG3, this is not necessary.
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Referee #1
Evidence, reproducibility and clarity
Very high evidence and clarity. Excellent scientific rigor.
The findings are important and reported clearly. The experiments are conducted in a rigorous way by numerous participating laboratories.
Significance
Very high significance, both from a molecular biology and clinical standpoints. This is an important manuscript that challenges the findings and conclusions of a prior high-profile paper in Science by Ma et al 2016, claiming that LAG3 is a receptor for aggregation-prone species of alpha-synuclein and that deletion of LAG3 results in reduced cell to cell propagation of alpha-synuclein aggregates.
The experiments in this paper are numerous and employ a variety of techniques. The overall conclusions are that LAG3 is not expressed by the relevant neurons and that LAG3 is not a receptor for alpha-synuclein fibrils (of different sizes). Therefore, the authors conclude that LAG3 is unlikely to play a role in the spread of alpha-synuclein pathology in Parkinson's disease and related disorders.
There are, however, some weaknesses. For example, the Introduction contains passages that are not written in a stringent way:
- "Histologically, PD is characterized by α-synuclein aggregates known as Lewy Bodies in neurons of the substantia nigra," That is not a good description of PD neuropathology. Lewy pathology is present in numerous areas of the CNS and PNS, and is not restricted to the substantia nigra.
- "Growing evidence suggests that α-synuclein fibrils spread from cell to cell". While alpha-synuclein pathology can spread from cell to cell, it is not known if the fibrils are the species (alone or combined with other conformers) that cause the spreading of the pathology in a seeding fashion, or if smaller alpha-synuclein assemblies play that role.
- "...by a "prionoid" process of templated conversion (Aguzzi, 2009; Aguzzi and Lakkaraju, 2016; Jucker and Walker, 2018; Kara, Marks and Aguzzi, 2018; Scheckel and Aguzzi, 2018; Uemura et al., 2020)." This sentence gives the impression that the corresponding author has led the field when it comes to alpha-synuclein's prionid properties. That is not really the case, and it would be appropriate to cite the literature in a more scholarly fashion that reflects how this part of the alpha-synuclein research field developed.
- "Interrupting transmission of a-synuclein may slow down or abrogate the disease course." This is a bold statement and far from certain. While one might propose that this is the case, it is still just a hypothesis and the Introduction should reflect that.
Referee Cross-commenting
I concur with reviewers 2 and 3, and the new comment from reviewer 2. This paper should be published as soon as possible.
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Reply to the reviewers
The authors do not wish to provide a response at this time.
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Referee #3
Evidence, reproducibility and clarity
In this paper, Dr. Tanenbaum and colleagues present a new method to determine the exact point of the cell cycle in which a cell is. This new method has the potential to be applied to any cell-cycle phase and even to other processes. Focusing on M-G1 transition, they do sequencing of single human cells. They identify two groups of cell cycle-related genes, expressing mRNAs which are degraded either immediately after exit from mitosis or later on during G1. One of the factors involved in this degradation is identified as CNOT1.
In my opinion, the new method is well stablished and has the potential to be very useful to future work. In general, I think that the main conclusions are based on more than one approaches and are convincing. In relation to these, I have two major concerns:
- Although it is clear that a scheduled mRNA decay exits, this does not exclude the possibility of a concomitant effect on mRNA synthesis. A measurement of nascent transcription is needed.
- As mentioned in the discussion, it is possible that the limited effect of depleting CNOT1 is due to the partial knockdown. However, it is also possible that a different pathway of mRNA degradation is involved. This should be addressed by targeting other decay factors (for example Xrn1 and/or an exosome component).
Minor comments:
- Cell cycle control is not absolutely universal. The authors should mention that their results and conclusions correspond to human cells; if not in the title, at least in the abstract.
- Is SORT-seq (mentioned exclusively in the methods section) the same as scRNA-seq?
- Figure 2: there is no correspondence between the TOP2A images and their quantification. This experiment also needs an unrelated mRNA FISH as a negative control.
- Figure 3D: if I correctly understood this experiment, "Time in Actinomycin D" is a better title for the X axis. "Time after mitotic shake-off" is misleading because it suggests that the cells were released from the mitotic blockage.
- Figure S3L: the blockage of transcription by Actinomicin D should be demonstrated by a more general method, such as EU (5-ethynyl uridine) incorporation.
- Figure 4A: what is the cell cycle phenotype of CNOT1 siRNA? If a reduction with CRISPRi of 50 % causes a phenotype (Figure S4C), then a reduction of 90 % by the siRNA (Figure S4A) should cause a stronger phenotype.
- Do the two waves of protein degradation (mentioned in the second paragraph of page 12) affect the same genes than the two waves of mRNA degradation?
Significance
The new method described in this paper could be useful to address many questions in the field of cell-cycle control. Moreover, with modifications, it could be applied to any time-dependent biological problem. In addition, the scheduled degradation of mRNAs in the M-G1 transition is a discovery of biological significance.
In my opinion, the paper is technically interesting to a broad range of investigators, and biologically relevant for those studying the cell cycle.
Keywords of my field of expertise: transcription, chromatin, gene expression.
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Referee #2
Evidence, reproducibility and clarity
Summary:
In this study Krenning, Sonneveld, and Tanenbaum have investigated the temporal control of mRNA decay after mitosis. Previous work has demonstrated that following mitosis, regulated protein degradation serves an important role in erasing any lingering memory of the previous cell cycle. Left unanswered however, is whether mRNA decay is similarly regulated after mitosis, and if so, what role does it play in the cell cycle. The authors use time-lapse imaging and single-cell RNAseq to measure decay rates of mRNAs after mitosis. They use the FUCCI sensors to identify the precise age of each individual cell prior to performing single-cell RNAseq. Using this pseudo-timelapse approach, they identify several genes that are actively degraded after mitosis. Interestingly, they find that some mRNAs are decayed rapidly and immediately after mitosis while other mRNAs are decayed only after a delay of about 1.5 hours after mitosis. The authors find that, at least for several of the genes, the protein CNOT1 mediates the decay. The authors conclude that regulated mRNA decay occurs after mitosis and helps reset the transcriptome at the onset of a new cell cycle.
The question being asked in this manuscript is interesting and potentially very important to the cell cycle field. However, I believe this study suffers from several technical issues highlighted below as well as relatively modest effect sizes, particularly when it comes to ascribing CNOT1 as the key regulator mediating mRNA decay upon mitotic exit.
Major Comments:
1) The authors repeatedly claim that they can accurately measure the time a cell has spent in G1 phase, due to using live-cell imaging to calibrate their FACS data. However, following mitosis, cells bifurcate into either G0/Quiescence or into G1 phase. Importantly, the FUCCI-G1 sensor is not capable of distinguishing between these two cell cycle phases. Thus, while two cells may have spent the same amount of time since mitosis, one cell may be in Quiescence while the other cell is in G1 phase and they would both have the same level of FUCCI-G1. Even by live-cell imaging its not possible to distinguish between these two cell cycle phases with the markers used in this study. I believe you can see evidence for this in the Flow cytometry data in Figure 1C where there is a large population of cells with very high FUCCI-G1 levels (even higher than most of the S phase cells) but very low FUCCI-G2 levels. These cells likely represent cells that entered G0 after mitosis, remained there for several hours, and thus accumulated very high levels of the FUCCI-G1 sensor. This technical limitation has several implications. First, it means what is likely going into the single-cell mRNA seq workflow is a mixture of G0 and G1 cells. Since the authors observe two distinct "waves" of mRNA decay, it makes me wonder if one wave might be occurring in G1 cells while the other wave is occurring in G0 cells? Second, the authors state several times they can accurately determine the time a cell has spent in G1 phase. The more accurate statement however is that the authors can accurately determine the time that has elapsed since mitosis, since they cannot distinguish between G0 and G1 phase. This is admittedly a nuanced distinction but an important one given that quiescence cells are in a very different cellular state than cells in G1 phase. The authors actually use the correct x-axis label of "Time after metaphase (min)" in several of their figures, but they do not use the same language in the main text or to describe their conclusions. To overcome the technical challenge of distinguishing between G0/G1 cells and to address these two points, the authors could use an additional FUCCI sensor, mVenus-p27K(-), which accumulates in G0 cells but not in G1 cells (PMID: 24500246).
2) One of the main novelty claims of the paper is that mRNA decays following mitotic exit in two waves. In order to support this claim, the authors plot the time since metaphase vs normalized transcripts for many single cells. For several genes including CDK1, TOP2A, and UBE2C, there is an immediate drop from time 0 to the next most densely populated timepoint of about 20 minutes. This results in a bimodal histogram as seen in Figure 2A, where there is one single bin representing genes that are maximally decayed at time 0, while another population is more normally distributed with a median decay time of ~80minutes. I have two concerns about this data. First, there are very few if not zero cells analyzed that were between 0 and 20 minutes old at the time of collection. Therefore the authors do not know if the mRNA decayed immediately after mitosis or with a 20minute delay after mitosis. Thus, rather than some genes decaying immediately after mitotic exit resulting in that one bin at time=0 and some genes decaying with a delay, there could actually be just one wave of mRNA decay that is broadly and normally distributed from 20-80minutes after mitosis (see histogram Figure 2 and Figure S3G; if you ignore anything less than 20minutes due to lack of data during this time window, then there is just a single distribution). While likely technically challenging due to cytokinesis, sampling cells that are between 0-20minutes old may be important to accurately measuring the decay rates of mRNAs upon mitotic exit. Second, its not entirely clear from the methods section, but I am assuming that for time 0 of the plots in Figure S3A-F, the authors are using G2/M sorted cells as defined by FUCCI-G2 high/FUCCI-G1 low status. However, depending on what precise FACS gates were used to do this sort, these cells could be anywhere in early G2, late G2, prometaphase, metaphase, etc and they are all averaged together. Thus, when the authors claim that the mRNAs are decaying immediately after mitosis, that's based on comparing the mRNA levels in this mixed G2/M population with cells that are 20minutes or more after mitosis. For genes like CDK1 where the mRNA is almost completely gone at 20 minutes after mitosis when they first have any cells to measure, its entirely possible these mRNAs were already decayed either before or within mitosis, rather than upon mitotic exit. What we really need to know is what are the mRNA levels precisely at metaphase and plot that value as time=0 (for example in figure S3A-F). Perhaps the authors could use CDK1i plus Taxol treatment to accumulate cells in mitosis like they describe in the methods for the transcription inhibition experiments. (If this is what was done for the Sort-Seq experiments as well as the data in Fig S3A-F, my apologies for not completely understanding, but the methods section should be updated to make this more clear)
3) As the authors point out in the discussion, the effect size of CNOT1 depletion on mRNA decay are rather small. Notably the genes that appear to be statistically significant are all the genes that are hardly decayed after mitosis anyways (see Figure 4D, ARLGIP1, PSD3, etc). These genes appear to be only down about 2-fold (-1 on a log2 scale axis) in the control group, which would be expected during mitosis when the mother cell splits in half into two daughter cells. Depending on the method of normalization, this change in mRNA levels may simply be due to this. I understand the technical limitations in knocking down an essential gene, but given that one of the major novelty claims of this study is that CNOT1 mediates the mRNA decay upon mitotic exit, more robust proof is warranted. The authors could employ the inducible protein degradation system they referenced in the discussion. Additionally they could perhaps show data that CNOT1 is somehow differentially regulated during mitotic exit that would account for this sudden change in mRNA stability. If the authors were to include additional corroboratory data demonstrating CNOT1 is most active during mitotic exit for example, it would help to overcome that low effect size upon mild CNOT1 depletion.
Minor comment:
1) The authors state that they can "accurately determine the time a cell has spent in G1 phase based on its FUCCI-G1 fluorescence as measured by FACS" (Page 6, last line of the first paragraph). It would be nice to know how accurately? What is the level of uncertainty in your measurements? +/- how many minutes?
2) The authors only focused on those genes whose mRNA's were decayed upon mitotic exit, but of equal interest would be those cell cycle genes that were not observed to decay upon mitotic exit. The authors may want to highlight these genes, because it might shed light on what aspects of the cell cycle cells want to reset, and what aspects of the cell cycle the cells may wish to "remember" from the previous cell cycle. For example, what is the status of the cyclins? CIPs? Origin licensing genes? There is growing evidence that the status of the mother cell can influence the cell cycle of the daughter cell and mRNA levels of key cell cycle genes have been implicated in this (PMIDs: 28514656, 28317845, 28869970).
Significance
This paper offers a potential conceptual advance to our understanding of how cells reset after the cell cycle is completed. By demonstrating that cells regulate protein as well as mRNA degradation upon cell cycle exit, the authors show cells utilize multiple mechanisms to reset the biochemical state of the cell at the onset of a fresh cell cycle. This work would be of potential interest to the cell cycle field, particularly those interested in G1 regulation. It would also be of interest to people interested in mRNA regulation as it would demonstrate a clear window during which mRNA decay was specifically upregulated.
While my expertise lies in the cell cycle and the use of FUCCI sensors to identify cell cycle stages, I have less expertise in single-cell RNAseq and methods of mRNA quantification.
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Referee #1
Evidence, reproducibility and clarity
In the manuscript "Time-resolved single-cell sequencing identifies multiple waves of mRNA decay during mitotic exit", Krenning et al. describe a method that connects live-cell microscopy with single-cell RNA sequencing in order to monitor global changes in mammalian mRNA gene expression in a cell-cycle-dependent manner. To this end they employ a fluorescent, ubiquitination-based cell cycle indicator (FUCCI system) in human untransformed RPE-1 cells coupled to SORT-Seq in order to generate a high-resolution, time-resolved transcriptome profile of cells spanning the transition form M phase into G1 phase. By comparing FACS-based sampling with an in silico trajectory inference method the authors provide convincing evidence that this system allows for high-resolution, time-resolved transcriptome profiling of cells in the transition from M-phase into G1 phase. Subsequent analysis of changes in steady-state gene expression revealed a set of >200 transcripts that undergo rapid decay in two distinct waves, first around the time of mitotic exit and second upon G1 entry. Those results were independently validated by single molecule FISH of select transcripts, revealing that the first wave of RNA decay initiates at the start of anaphase and the second wave starts during early G1 phase. Using mathematical modeling followed by selective validation (using cell-cycle staging combined with global inhibition of RNA decay), the authors derive and confirm precise mRNA decay rates for cell cycle regulated mRNAs that were overall lower than what has been observed in previously described population-based half-life measurements. Finally, the authors establish a role of deadenylation by the CCR4-NOT complex in selective mRNA decay during M-phase/G1 transition by revealing a partial stabilization upon NOT1-depletion by RNAi.
I have only a minor comment to help improve the mechanistic insights: While the authors attribute the partial stabilization of cell-cycle regulated mRNAs to an incomplete depletion of NOT1 (which is possible), an alternative hypothesis would be that decapping and 5´-to-3´ decay further contribute to mRNA turnover. Notably, the authors describe the use of siRNAs targeting Dcp2 in the methods section (without referring to it in the results part), indicating that they may have data that could clarify this. They authors may consider adding this data to complete an otherwise nicely executed and well-written manuscript.
Significance
Overall, this is an impressive and well-controlled body of work providing novel insights into cell-cycle controlled mRNA decay. It reveals novel insights into the targets and molecular mechanisms of mRNA decay in the transition of mitosis to G1, thereby adding significantly to our understanding of the scope of tightly controlled gene expression for proper execution of the cell cycle.
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Reply to the reviewers
Rebuttal letter – Response to Reviewers
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
This study focused on P. vivax, which is an important neglected human malaria killer. The reported evidence will have a significant impact on diagnosing infectious diseases. The language in the manuscript is very good. However, some typos were reported. Some paragraphs might need particular attention to punctuation. Overall, the work is very good. The statistics are straight forward. However, there are a couple of major points that must be addressed before publication. Some of my comments are just recommendations to clarify some sections of the text.
**Major comments:**
The statistical methods can be improved by using generalised mixed models (GLMM).
1- PCA graphs need to be organised in more descriptive ways. Dim1 and Dim2 in each axis need to be defined clearly in the figures. PCA in Fig2 c is very difficult to follow, and it needs to be organised.
Answer: Figures have been amended to be more self-explanatory and clearer to the reader.
2- In this study, patients were male and female, and we know already male and female haematological parameters are hugely different, specially Hb level, and so on. My question is how the sex variable is treated in this study? Did your control group were from both sexes? Sex could be treated as a random variable in all studies if GLMM models were used.
Answer: Information in how the sex variable was treated in the study has been added to the methods section. In our cross-sectional study with uncomplicated P. vivax malaria patients seen at FMT-HVD in Manaus, Brazil, patients and healthy donors (controls) were matched by age and sex. In both groups, frequency of female individuals was 30% and male individuals 70%.
We think sex is better fitted as fixed effect since only two levels for this factor are possible. Thus, we used linear models with age and sex as fixed variables for statistical testing and to ensure that the differences observed between P.vivax- infected patients and controls, as well as between the clusters, were only due to disease status. This analysis showed that red blood cells count, hemoglobin, hematocrit, MXD and neutrophils counts (this parameter only when comparing the clusters) needed to be corrected only due to sex influence. For these parameters, estimates of predicted sex influence were subtracted from the raw parameter values and residuals were used for statistical testing. We have added this information in the Methods section as indicated below:
Page 6, line 128: Patients and healthy donors were age and sex-matched, with a frequency of 30% female and 70% male individuals in both groups.
Page 14, line 336:
To ensure that differences observed between P. vivax - infected patients and controls, as well as between the clusters, were due to disease status and not confounded by age or sex, the clinical parameters were fitted as response variables in a linear model with sex and/or age fitted as explanatory variables. Age and sex were included in the model if their coefficients were estimated as different from zero with p-value The residuals from the linear model were then used as age and/or sex corrected parameters in subsequent analyses.
3- Why 6h and 18h used for the HUVEC evaluation?
Answer. We ran several optimization experiments with individual plasma samples where we observed maximal mRNA expression changes after 6h of stimulation. For experiments detecting protein expression (IFA and flow cytometry), we increased the stimulation time to 18h. Preliminary experiments suggested this to be the optimal duration without compromising cellular viability.
4- It is mentioned only neutrophil enriched in this study, if myelopoiesis is affected, why the other granulocytes were not showed significant enhancement?
Answer: Our data reveal no change in the number of circulating neutrophils in the different clusters of individuals. However, mixed cell counts (MXD), a parameter representing monocytes, basophils and eosinophils numbers, was significantly reduced in Vivaxhigh patients. As a result, there was a significant enrichment of neutrophils in the leukocyte fraction in the blood of Vivaxhigh patients as well as a higher Neutrophil:Lymphocyte count ratio (NLCR) (Figure 4). In hematopoietic progenitors, stochastic changes in each factor’s concentration could result in one factor’s becoming more abundant and committing a hematopoietic progenitor to a particular lineage. To generate each mature granulocyte population (e.g. basophils, eosinophils and neutrophils), common myeloid precursor cells (CMPs) and later precursors for granulocytic and monocytic lineages (GMPs) follow in the BM different lineage commitment programs, tightly-regulated or instructed by a specific set of soluble factors, cell-cell interactions and transcription factors, that define cell fate decisions and lineage restrictions. For instance, differential PU.1 activity can specify different cell fates during haematopoiesis regulating monocyte and neutrophils differentiation. Genetic and biochemical analyses have shown that G-CSF can direct granulocyte differentiation by changing the ratio of C/EBPα to PU.1 (Zhu et al., Oncogene 2002; Friedman Oncogene 2002; Dahl et al., Nat Immunol 2003). High expression levels of PU.1 and C/EBPa, stimulated by G-CSF, promote GMP differentiation to neutrophils and inhibits monocyte differentiation, while only PU.1 expression, IRF-8 and lower expression/activity of C/EBPs induce GMP differentiation to monocytes (Zhu et al., Oncogene 2002; Friedman Oncogene 2002; Dahl et al., Nat Immunol 2003). Meanwhile, a combination of PU.1, C/EBPb and low levels of GATA-1 differentiates GMPs to eosinophil lineage (Kulessa et al., 1995; McDevitt et al., 1997; Yamaguchi et al., 1999) and PU.1 must also cooperate with GATA2 to direct mast cell differentiation (Walsh et al., Immunity 2002). In addition, eosinophil and basophil differentiation are induced by a different set of cytokines, usually produced in prevalent T-helper 2 response, such as IL-5, which should be inhibited in the strong Th1 environment evidenced by our and previous Luminex data in Pv patients. The enrichment of activated neutrophils in the peripheral circulation of P. vivax patients could be due to a response that specifically enhances neutrophil production and release from the bone marrow (BM). This hypothesis is supported by emerging evidence for enrichment of P. vivax parasites in the hematopoietic niche of BM, our Luminex data showing significant increase in pro-inflammatory cytokines associated with emergency myelopoiesis (e.g., TNF-a, IL-1a, IL-1b, IL-6, IL-8), and increased circulating levels of G-CSF, the major inducer of neutrophils production in the BM. Likewise, increased activation-induced cell death (AICD) in T cells, splenic T-cell and platelet accumulation or decreased lymphopoiesis due to myeloid-biased HSC differentiation induced by inflammatory cytokines and EC activation in the BM (refs 36,37,39) might explain the neutrophil enrichment in vivax patients.
5- I would also ask the authors to speculate a bit on, What could be the mechanism behind the different function of P. vivax compared to P. falciparum? From an evolutionary perspective, the parasite should rather become softer and keep the host alive for its own benefit.
Answer: One of the characteristics of P. vivax that could play an important role in immunity is its restriction to invade immature reticulocytes. For example, the infected reticulocyte could play a role in the presentation of parasite antigens as reticulocytes (but not mature RBCs) express MHC-I and are capable to process and present antigens on their surface for recognition by T cells. Indeed, it has been shown that reticulocytes act directly as an antigen-presenting cell, emphasizing the importance of erythrocyte surface antigens both in the induction as well as the target of a protective immune response (Burel et al 2016, Junqueira et al 2018). Recent investigations comparing P. vivax and P. falciparum controlled human infection models (CHMIs) also revealed marked differences in the immune profiles generated following infection with the two species and postulated that protective immune responses to Plasmodium are species-specific. It has been hypothesized that this difference is due to strict P. vivax tropism for MHC-I-expressing reticulocytes that, unlike mature red blood cells, can present antigen directly to CD8+T cells. Specifically, P. vivax but not P. falciparum infection led to the expansion of a specific subset of CD38+CD8+ T cells which were associated with an activated phenotype and cytotoxic potential. Corroborating Burel et al findings in the CHMI model, Junqueira et al showed that P. vivax–infected reticulocytes express HLA-I. In P. vivax-infected patients, CD8+ T cells in the peripheral blood express high levels of cytotoxic proteins, recognize and form immunological synapses with P. vivax–infected reticulocytes in HLA–dependent manner. Next, it was showed that P. vivax-specific CD8+ T cells release their cytotoxic granules to kill both host cell and intracellular parasite, which prevented reinvasion (Junqueira et al 2018). Although these data indicate a protective role of cytotoxic CD8+ T cells during P. vivax blood-stage malaria, it is not clear whether these lymphocytes would always be beneficial because they might contribute to anemia, inflammation or other pathological sequelae of infection, which needs to be further investigated.
**Minor comments:**
It is important to have a reference, version, and date for the R software, packages and GraphPad.
Answer: We have added version and date for the R and GraphPad software.
2- In Fig 5, E missed to report. This figure can be better organised. It is very hard to read and follow.
Answer: There is no E in Figure 5. We will organize the figure to make it easier to read and follow.
Reviewer #2 (Significance (Required)):
- vivax remains endemic in 51 countries across Central and South Americas, the Horn of Africa, Asia and the Pacific islands. In most areas it is co-endemic with P. falciparum, which has been the priority species to address for national malaria control programmes. Malaria related deaths are mostly attributable to the more pathogenic P. falciparum, but over the last decade these have declined, however there has been a consistent rise in the proportion of malaria cases due to P. vivax. However, because it is difficult to diagnose resistant strains, strategies to detect and track drug resistant P. vivax* are limited. In this context it is vital to develop better tools to assess diagnostic, antimalarial efficacy and drug susceptibility so that emerging drug resistance can be tracked, and novel treatment strategies explored. From my viewpoint, despite some statistical problems to understand the complex nature of data (mixed interactions among multiple variables), these findings seem to be very interesting and (after a major revision) worth to be published. As said before, the story told by the authors could become interesting.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
The manuscript titled: "Total parasite biomass but not peripheral parasitaemia is associated with endothelial and haematological perturbations in Plasmodium vivax patients" by Silva-Filho et al., reinforce the original observation and data by the group of Nicholas Anstey and coworkers, who first proposed the use of plasma parasite lactate dehydrogenase and PvLDH as a marker of parasite biomass. In that work, it was already demonstrated that P. vivax biomass is related to plasma concentration of LDH levels. As such, the present work cannot be considered of high novelty. Yet, through a meticulous approach including clinical data, computational approaches, machine learning, LDH measurement, multiplex analysis and quantitave RT-PCR, the authors here have extended the original observations that a large biomass of P. vivax parasites is out of blood circulation. In contrast, unlike the original observations of Anstey´s group, a correlation between total parasite biomass and systemic levels of markers of endothelial cells activation, was observed. The manuscript is very well written and the discussion brings new knowledge in this key topic for elimination of malaria. This manuscript is therefore recommended for publication after the following comments are addressed.
**Major comments:**
The vascular endothelium plays a pivotal role in malaria. Therefore, to test whether cell and/or parasite factors affect the vascular endothelium, HUVEC cells were used in this study. This is of major concern as endothelial cells from the bone marrow, where most hematological disturbances, notoriously thrombocytopenia, occur, were not used instead. HUVEC cells seems the only endothelial cell that does not express ABO blood group antigens, thus suggesting that surface expression on these cells is highly altered (O´Donnell et al., 2000 J Vasc Res). Moreover, significant functional differences between HUVEC cells and adult vascular endothelium have been reported (Chan et al., 2004). Together, this indicates that results obtained with HUVEC cells might not reflect responses of the bone marrow vascular endothelium. As one of the corresponding authors have ample experience with working with human bone marrow endothelial cells (Mantel et al., 2016 Nat Comm), it is suggested to perform some experiments with these cells to assure extrapolation of the results obtained with HUVEC cells.
Answer: We agree with the reviewer that performing ex vivo assays with primary human bone marrow endothelial cells would be an excellent alternative. However, we would like to argue that HUVECs are also suitable for our purposes. HUVECs are widely used to study endothelial barrier function, for example in the context of angiogenesis and inflammatory responses/barrier disruption. To emphasise this point, we have now referenced examples where HUVECs were used in the context of endothelial barrier biology and in different inflammatory conditions (see also lists a, b, c below).
- Papers showing the use of HUVECs in studies yielding important insights about endothelial barrier function
- Krispin S et al. Growth Differentiation Factor 6 Promotes Vascular Stability by Restraining Vascular Endothelial Growth Factor Signaling. Arterioscler Thromb Vasc Biol. 2018.
- Aranda JF et al. MYADM controls endothelial barrier function through ERM-dependent regulation of ICAM-1 expression. Mol Biol Cell. 2013.
- Orsenigo F et al. Phosphorylation of VE-cadherin is modulated by haemodynamic forces and contributes to the regulation of vascular permeability in vivo. Nat Commun. 2012.
- *
- Papers that used HUVECs in studies about endothelial barrier function in inflammatory conditions
- Dickinson CM et al. Leukadherin-1 ameliorates endothelial barrier damage mediated by neutrophils from critically ill patients. J Intensive Care. 2018.
- Kuck JL et al. Ascorbic acid attenuates endothelial permeability triggered by cell-free hemoglobin. Biochem Biophys Res Commun. 2018.
- Tramontini Gomes de Sousa Cardozo F et al. **Serum from dengue virus-infected patients with and without plasma leakage differentially affects endothelial cells barrier function in vitro. PLoS One. 2017.
- Fox ED et al. Neutrophils from critically ill septic patients mediate profound loss of endothelial barrier integrity. Crit Care. 2013.
- Rahbar E et al. Endothelial glycocalyx shedding and vascular permeability in severely injured trauma patients. J Transl Med. 2015.
- *
- Papers showing that HUVECs behave similarly to other endothelial cell types in regard to barrier function, except when the comparison is with blood brain barrier models
*
Totani L et al. Mechanisms of endothelial cell dysfunction in cystic fibrosis. Biochim Biophys Acta Mol Basis Dis. 2017, Dec;1863(12):3243-3253.
- Gündüz D et al. Effect of ticagrelor on endothelial calcium signalling and barrier function. **Thromb Haemost. 2017 Jan 26;117(2):371-381.
- Deitch EA et al. Mesenteric lymph from rats subjected to trauma-hemorrhagic shock are injurious to rat pulmonary microvascular endothelial cells as well as human umbilical vein endothelial cells. ** 2001 Oct;16(4):290-3. Importantly, we were able to reproduce in the HUVEC ex vivo assays a phenotype of endothelial perturbations that is inferred based on the in vivo Luminex data using the same plasma sample. These data also support our hypothesis that patients with higher parasite biomass present higher endothelial cell perturbations, corroborating the associations between parasite accumulation in deep tissues (total parasite biomass represented by PvLDH levels) and endothelial cell activation as demonstrated in the Figure 6.
Strikingly, the authors stated that "P. vivax infection results in different ranges of EC alterations without massive cytoadhesion". This statement has no data supporting it. In fact, their own flow cytometry data convincingly demonstrated that exposure of HUVEC cells to plasma of vivax-high patients significantly increased the surface expression of ICAM-1 and VCAM. ICAM-1 expression is a well know receptor for cytoadhesion in malaria and Dr. Costa first demonstrated the importance of this receptor in cytoadherence of P. vivax (Carvalho et al., 2010). Moreover, these data are in some contradiction with the original observations of Anstey and collaborators who demonstrated that parasite LDH concentration did not correlate with markers of endothelial activation (Barber et al., 2015 PLoS Path). Therefore, this sentence should be modified to accommodate the alternative possibility of cytoadherence, deleted from the manuscript or binding functional assays should be performed to sustain it.
Answer: We agree with the reviewer and have removed this statement.
Page 22, line 543: The association between endothelial activation, Syndecan-1 and parasite biomass (PvLDH) indicates a positive feedback loop between glycocalyx breakdown, activation of endothelial receptors such as ICAM-1and VCAM-1 and parasite accumulation in deep tissues9,12.
Extracellular vesicles are key players in pathology of malaria and this includes P. vivax where concentration of circulating microparticles were associated with acute infections (Campos et al., 2010 Mal J). Moreover, Dr. Marti has pioneered this field since the original manuscript describing the role of EVs in malaria as intercellular communicators (Mantel et al., 2013 Cell). More recently, his group also demonstrated that interaction of EVs with bone marrow endothelial cells induce expression of IL-6 and IL-1 as well as vascular endothelium perturbations after trans-endothelial electrical resistance experiments (Mantel et al., 2016 Nat Comm). Furthermore, another recent report showed the physiological role of EVs in vivax malaria by demonstrating that EV uptake by human spleen fibroblast induced nuclear translocation of the NF-kB transcriptional factor, concomitant with surface expression of ICAM-1, thus facilitating cytoadherence of infected reticulocytes from P. vivax patients (Toda et al., 2020 Nat Comm). This growing evidence indicates that plasma circulating EVs are key communicators in malaria infections potentially explaining some of the findings reported in this work. Neglecting the importance of EVs in the discussion of this article is not reasonable and weakens this manuscript. Including a paragraph on EVs and accurate references in the discussion is thus strongly recommended.
Answer: We agree with the reviewer that extracellular vesicles are key communicators in malaria infection. We have not measured them in our study, however, and therefore can only speculate about their impact on our observations. We have added a phrase in the discussion:
Page 27, line 661: It is likely that other circulating factors that we have not directly measured in our study are also contributing to EC activation and vascular permeability. In particular, extracellular vesicles (EV) originating from ECs, platelets, and RBCs are present during malaria infection and are known to modulate the host immune response to the parasite54-56 . In P. falciparum, infected RBCs release EVs containing immunogenic parasite antigens, that activate macrophages, induce neutrophil migration and alter endothelial barrier function54,55. In P. vivax, plasma-derived EVs from iRBCs are taken up by human spleen fibroblasts (hSFs). This event signals NF-kB translocation and upregulation of ICAM-1 expression, facilitating cytoadherence of P. vivax-infected reticulocytes56.
**Minor comments:**
The lack of a group including severe vivax malaria patients is a drawback of this article as this group would have firmly validated the predictor of severe disease.
Answer: This study was investigating a cohort of uncomplicated P. vivax malaria compared to controls. We agree that it will be important to extent our analysis to severe vivax malaria in future studies.
In the selection criteria of the patients to be included in the study, no information on other co-infections were mentioned. Is this information available? If so, this should be mentioned.
Answer: As described in the Methods sections, Page 6, line 132, mono infection by P. vivax was confirmed by analysis of blood smears and quantitative PCR (qPCR) for both P. vivax and P. falciparum. We agree that excluding other coinfections could have been of interest. However, the differential diagnosis for an acute febrile illness is very broad and it would be impractical to track all other possible diseases. In addition, the patients included in the present work had mild disease, and therefore were discharged from hospital after a positive malaria diagnosis. No further investigation on other infections was done.
The main coinfection to be considered for an acute febrile illness with no localizing signs in our context is Dengue Fever. Although Dengue coinfection in our cohort is possible, the incidence at the Hospital is only 2.8% (P. vivax/Dengue coinfection) (Magalhães et al, Plos NTD 2014). Thus, it is unlikely that such a coinfection would have a major impact on our findings.
This work determined the levels of PvLDH in a cohort of uncomplicated P. vivax patients as well as healthy volunteers using a double-sandwich ELISA assay: (i) are the clones to determine PvLDH values freely available to facilitate similar studies by independent groups? (ii) How was the cut-off of positivity defined? This is not evident, neither in the materials and methods, nor in the results.
Answer: Clones are commercially available and were purchased from Vista Diagnostics International LLC, WA, USA. Information has been amended to the text in the Methods section.
Page 8, line 186: “Cut-off of positivity was defined by correcting absorbance values generated in the plasma samples from healthy donors (controls) by blank values (plate controls), with both values being in the same range. Absorbance values higher than controls were considered positive. In parallel, we used schizont extracts to perform standard curves and lower absorbance values were in the range of O.D = 0.03-0.04. All positive patient samples gave O.D. values equal or higher than 0.05. This information has also been added in the Methods section.:
It is not clear why varying percentages of pooled plasma (30% for imaging and flow cytometry, and 20% for impedance changes) from the different clusters were used for the functional EC assays. Moreover, no information about the concentration of plasma used for transcriptional analysis is available. Please clarify.
Answer: The concentration of 30% pooled plasma was also used for transcriptional analysis, as indicated in the Methods section, page 11, line 250. This information was also added in the legend of Figure 5B. We had run several optimisation time-course and titration experiments with individual plasma samples, testing concentrations of plasma varying from 10% up to 30% v/v and we did not observe differences in mRNA expression between 20% and 30% v/v plasma conditions.
As for the ECIS, our collaborators (Erich V de Paula group) have optimised this assay and they use a range of 15 to 20% (Santaterra et al 2020). Higher concentrations of plasma reduces the reproducibility, probably to fibrin formation.
Reference 9 is a nonhuman primate study where no LDH is used. Please remove it.
Answer: Reference 9 has been removed following the reviewer suggestion.
Reference 39 is a review on the subject and cannot be included in the sentence on line 556 "In agreement with a previous study8,39, where reference 8 is accurate. Please remove reference 39 from here.
Answer: The text has been amended as suggested.
Reviewer #3 (Significance (Required)):
This paper further contributes to explain the conundrum of low peripheral blood parasitemia and clinical severity in P. vivax. Moreover, by including new human markers and solidly applying computational tools, this paper further contributes to advance clinical research in P. vivax.
Clinical diagnosis of hematological disorders including anemia, lymphopenia and thrombocytopenia, are routinely obtained from a complete blood count. Therefore, I believe the major significance of this work is to raise public health awareness of including in these clinical examinations, the determination of PvLDH levels. They might prognose, as suggested by the authors, better diagnosis and treatment of P. vivax,
My main expertise is the biology of host-pathogen interactions with a focus on P. vivax.
Reviewer #4 (Evidence, reproducibility and clarity (Required)):
The study evaluates P. vivax biomass (serum LDH) versus peripheral parasitemia with multiple variables. From the biomass Vivax high vs. Vivax low, they compare multiple determination in patients with uncomplicated P. vivax. This raises questions about disease and the presence of parasites in various organs. The question is if P. vivax sequesters and the answer is yes in the bone marrow and spleen. Does it sequester like P. falciparum that causes disease by sequestration by binding endothelium in various organs. That is less clear. As P. vivax is rarely fatal, the sequestration has not been studied. The presence of parasites in organs of P. vivax infected splenectomized squirrel and Aotus monkeys has been found in bone marrow and liver (note: splenecotomized monkeys so parasitemia can rise to higher levels than in non-splenectomized monkeys). There are studies of binding of schizonts infected red cells to lung endothelium in vitro does not answer the question of whether sequestration occurs in vivo.
The most important complication of P. vivax is generally anemia. This did not correlate with vivax biomass, but this raises the question of the length of infection and the possibility that parasite biomass may vary at different times of infection. Anemia was seen in P. vivax infected patients, but it did not relate to biomass at the time of study. Note the caveat mentioned in the previous sentence on long term effects of infection on anemia.
The finding of biomass with reduced platelet counts and endothelial effects that may be related to a serum factor and not sequestration. This is the main limitation of the paper besides the unknown long term effect infection. If one could identify an effect of P. vivax infected human serum, this may be worth a study in the future on what is in serum causing the effects.
Reviewer #4 (Significance (Required)):
This study is unique with the caveats mentioned above. It has a good review of the literature.
Answer: We appreciate the reviewer comments. In our cohort, the frequency of anaemia was not as high or severe as the frequency of thrombocytopenia and lymphopenia. However, we still find associations between endothelial cell activation marker Ang-2 and the pro-inflammatory cytokine IL-1 IL-1 negatively associated with several markers of anaemia, such as haemoglobin, haematocrit and RBC numbers. Although we did not further investigate this association, it may indicate indirect effects of parasite biomass on anaemia mediated by inflammation and EC activation, which will be further investigated in other current longitudinal cohort studies.
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Referee #3
Evidence, reproducibility and clarity
The study evaluates P. vivax biomass (serum LDH) versus peripheral parasitemia with multiple variables. From the biomass Vivax high vs. Vivax low, they compare multiple determination in patients with uncomplicated P. vivax. This raises questions about disease and the presence of parasites in various organs. The question is if P. vivax sequesters and the answer is yes in the bone marrow and spleen. Does it sequester like P. falciparum that causes disease by sequestration by binding endothelium in various organs. That is less clear. As P. vivax is rarely fatal, the sequestration has not been studied. The presence of parasites in organs of P. vivax infected splenectomized squirrel and Aotus monkeys has been found in bone marrow and liver (note: splenecotomized monkeys so parasitemia can rise to higher levels than in non-splenectomized monkeys). There are studies of binding of schizonts infected red cells to lung endothelium in vitro does not answer the question of whether sequestration occurs in vivo.
The most important complication of P. vivax is generally anemia. This did not correlate with vivax biomass, but this raises the question of the length of infection and the possibility that parasite biomass may vary at different times of infection. Anemia was seen in P. vivax infected patients, but it did not relate to biomass at the time of study. Note the caveat mentioned in the previous sentence on long term effects of infection on anemia. The finding of biomass with reduced platelet counts and endothelial effects that may be related to a serum factor and not sequestration. This is the main limitation of the paper besides the unknown long term effect infection. If one could identify an effect of P. vivax infected human serum, this may be worth a study in the future on what is in serum causing the effects.
Significance
This study is unique with the caveats mentioned above. It has a good review of the literature.
-
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Referee #2
Evidence, reproducibility and clarity
The manuscript titled: "Total parasite biomass but not peripheral parasitaemia is associated with endothelial and haematological perturbations in Plasmodium vivax patients" by Silva-Filho et al., reinforce the original observation and data by the group of Nicholas Anstey and coworkers, who first proposed the use of plasma parasite lactate dehydrogenase and PvLDH as a marker of parasite biomass. In that work, it was already demonstrated that P. vivax biomass is related to plasma concentration of LDH levels. As such, the present work cannot be considered of high novelty. Yet, through a meticulous approach including clinical data, computational approaches, machine learning, LDH measurement, multiplex analysis and quantitave RT-PCR, the authors here have extended the original observations that a large biomass of P. vivax parasites is out of blood circulation. In contrast, unlike the original observations of Anstey´s group, a correlation between total parasite biomass and systemic levels of markers of endothelial cells activation, was observed. The manuscript is very well written and the discussion brings new knowledge in this key topic for elimination of malaria. This manuscript is therefore recommended for publication after the following comments are addressed.
Major comments:
- The vascular endothelium plays a pivotal role in malaria. Therefore, to test whether cell and/or parasite factors affect the vascular endothelium, HUVEC cells were used in this study. This is of major concern as endothelial cells from the bone marrow, where most hematological disturbances, notoriously thrombocytopenia, occur, were not used instead. HUVEC cells seems the only endothelial cell that does not express ABO blood group antigens, thus suggesting that surface expression on these cells is highly altered (O´Donnell et al., 2000 J Vasc Res). Moreover, significant functional differences between HUVEC cells and adult vascular endothelium have been reported (Chan et al., 2004). Together, this indicates that results obtained with HUVEC cells might not reflect responses of the bone marrow vascular endothelium. As one of the corresponding authors have ample experience with working with human bone marrow endothelial cells (Mantel et al., 2016 Nat Comm), it is suggested to perform some experiments with these cells to assure extrapolation of the results obtained with HUVEC cells.
- Strikingly, the authors stated that "P. vivax infection results in different ranges of EC alterations without massive cytoadhesion". This statement has no data supporting it. In fact, their own flow cytometry data convincingly demonstrated that exposure of HUVEC cells to plasma of vivax-high patients significantly increased the surface expression of ICAM-1 and VCAM. ICAM-1 expression is a well know receptor for cytoadhesion in malaria and Dr. Costa first demonstrated the importance of this receptor in cytoadherence of P. vivax (Carvalho et al., 2010). Moreover, these data are in some contradiction with the original observations of Anstey and collaborators who demonstrated that parasite LDH concentration did not correlate with markers of endothelial activation (Barber et al., 2015 PLoS Path). Therefore, this sentence should be modified to accommodate the alternative possibility of cytoadherence, deleted from the manuscript or binding functional assays should be performed to sustain it.
- Extracellular vesicles are key players in pathology of malaria and this includes P. vivax where concentration of circulating microparticles were associated with acute infections (Campos et al., 2010 Mal J). Moreover, Dr. Marti has pioneered this field since the original manuscript describing the role of EVs in malaria as intercellular communicators (Mantel et al., 2013 Cell). More recently, his group also demonstrated that interaction of EVs with bone marrow endothelial cells induce expression of IL-6 and IL-1 as well as vascular endothelium perturbations after trans-endothelial electrical resistance experiments (Mantel et al., 2016 Nat Comm). Furthermore, another recent report showed the physiological role of EVs in vivax malaria by demonstrating that EV uptake by human spleen fibroblast induced nuclear translocation of the NF-kB transcriptional factor, concomitant with surface expression of ICAM-1, thus facilitating cytoadherence of infected reticulocytes from P. vivax patients (Toda et al., 2020 Nat Comm). This growing evidence indicates that plasma circulating EVs are key communicators in malaria infections potentially explaining some of the findings reported in this work. Neglecting the importance of EVs in the discussion of this article is not reasonable and weakens this manuscript. Including a paragraph on EVs and accurate references in the discussion is thus strongly recommended.
Minor comments:
- The lack of a group including severe vivax malaria patients is a drawback of this article as this group would have firmly validated the predictor of severe disease.
- In the selection criteria of the patients to be included in the study, no information on other co-infections were mentioned. Is this information available? If so, this should be mentioned.
- This work determined the levels of PvLDH in a cohort of uncomplicated P. vivax patients as well as healthy volunteers using a double-sandwich ELISA assay: (i) are the clones to determine PvLDH values freely available to facilitate similar studies by independent groups? (ii) How was the cut-off of positivity defined? This is not evident, neither in the materials and methods, nor in the results.
- It is not clear why varying percentages of pooled plasma (30% for imaging and flow cytometry, and 20% for impedance changes) from the different clusters were used for the functional EC assays. Moreover, no information about the concentration of plasma used for transcriptional analysis is available. Please clarify.
- Reference 9 is a nonhuman primate study where no LDH is used. Please remove it.
- Reference 39 is a review on the subject and cannot be included in the sentence on line 556 "In agreement with a previous study8,39, where reference 8 is accurate. Please remove reference 39 from here.
Significance
This paper further contributes to explain the conundrum of low peripheral blood parasitemia and clinical severity in P. vivax. Moreover, by including new human markers and solidly applying computational tools, this paper further contributes to advance clinical research in P. vivax.
Clinical diagnosis of hematological disorders including anemia, lymphopenia and thrombocytopenia, are routinely obtained from a complete blood count. Therefore, I believe the major significance of this work is to raise public health awareness of including in these clinical examinations, the determination of PvLDH levels. They might prognose, as suggested by the authors, better diagnosis and treatment of P. vivax,
My main expertise is the biology of host-pathogen interactions with a focus on P. vivax.
-
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Referee #1
Evidence, reproducibility and clarity
This study focused on P. vivax, which is an important neglected human malaria killer. The reported evidence will have a significant impact on diagnosing infectious diseases. The language in the manuscript is very good. However, some typos were reported. Some paragraphs might need particular attention to punctuation. Overall, the work is very good. The statistics are straight forward. However, there are a couple of major points that must be addressed before publication. Some of my comments are just recommendations to clarify some sections of the text.
Major comments:
The statistical methods can be improved by using generalised mixed models (GLMM).
1- PCA graphs need to be organised in more descriptive ways. Dim1 and Dim2 in each axis need to be defined clearly in the figures. PCA in Fig2 c is very difficult to follow, and it needs to be organised.
2- In this study, patients were male and female, and we know already male and female haematological parameters are hugely different, specially Hb level, and so on. My question is how the sex variable is treated in this study? Did your control group were from both sexes? Sex could be treated as a random variable in all studies if GLMM models were used.
3- Why 6h and 18h used for the HUVEC evaluation?
4- It is mentioned only neutrophil enriched in this study, if myelopoiesis is affected, why the other granulocytes were not showed significant enhancement?
5- I would also ask the authors to speculate a bit on, What could be the mechanism behind the different function of P. vivax compared to P. falciparum? From an evolutionary perspective, the parasite should rather become softer and keep the host alive for its own benefit.
Minor comments:
1- It is important to have a reference, version, and date for the R software, packages and GraphPad.
2- In Fig 5, E missed to report. This figure can be better organised. It is very hard to read and follow.
Significance
P. vivax remains endemic in 51 countries across Central and South Americas, the Horn of Africa, Asia and the Pacific islands. In most areas it is co-endemic with P. falciparum, which has been the priority species to address for national malaria control programmes. Malaria related deaths are mostly attributable to the more pathogenic P. falciparum, but over the last decade these have declined, however there has been a consistent rise in the proportion of malaria cases due to P. vivax. However, because it is difficult to diagnose resistant strains, strategies to detect and track drug resistant P. vivax are limited. In this context it is vital to develop better tools to assess diagnostic, antimalarial efficacy and drug susceptibility so that emerging drug resistance can be tracked and novel treatment strategies explored.
From my viewpoint, despite the some statistical problems to understand the complex nature of data (mixed interactions among multiple variables), these findings seem to be very interesting and (after a major revision) worth to be published. As said before, the story told by the authors could become interesting.
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Reply to the reviewers
We thank the reviewers for their evaluation and are pleased that they appreciated both the significance and the novelty of our work, as well as the quality of its execution. Please find below a reply to the comments made by the reviewers.
To address the point raised by reviewer #1, we used a BY strain (from an S288C background), which is one of the most widely used lab strains in yeast genetics. Although a mutation in the HAP1 gene was identified in this strain, it does not compromise the ability of the cells to respire, as shown in our experiments performed in a non-fermentative medium in this manuscript (Fig. 2). Similarly, we have already published growth curves, drop tests, and proliferation rates of this strain in glycerol/ethanol or lactate-containing medium (please see Jimenez et al., JCS, 2014). More importantly, detailed respiration parameters have been measured for our BY background by the Daignan-Fornier lab, a long-standing Sagot lab collaborator (please see Gauthier et al., Mol Mic, 2008). Last, we have previously shown that upon quiescence establishment, there is no difference in mitochondrial network reorganization between BY/S288C and W303 or CEN PK background (Laporte et al., Elife, 2018, Fig2 SupFig1 F-G). Altogether, these results indicate that using this particular lab strain background does not detract from the generality of the observations reported in our manuscript. We will include a short discussion on this specific topic in the main text in a full revision.
Regarding reviewer #2’s comments, we are committed to providing all necessary details to fully replicate the microfluidic devices upon a final revision of our manuscript to make it widely accessible to the research community.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
These investigators have teamed up to solve a technical problem that has thwarted efforts to get a clear picture of the chronology of events in yeast cultures as they naturally exhaust their nutrient supply. This is a challenge because the time course is long and the density of the culture makes single cell analysis problematic. Previous studies involving abrupt starvation have shown that there is a pH drop when nutrients are eliminated, but abrupt starvation also leads to rapid loss of viability compared to what is observed with cells as they respond and adapt to changes in their environment. This microfluidic devise and an intracellular pH detector allowed them to follow pH change as cells transition from fermentation to respiration and stationary phase. About 15% of the population responds completely differently than the other 85%, making this single cell analysis crucial. It also provides a negative control of sorts, to further substantiate the correlations they draw. This 15% fails to enter the respiratory phase and dies rapidly. The pH also drops rapidly and is correlated with loss of mitochondrial function and aggregation of proteins. The 85% of cells that succeed in shifting to respiration suffer the same pH drop, but it is much slower and is correlated with slower protein aggregation, P Body, actin body, and proteosome storage Granule assembly. They also followed the cytoplasmic transition to a glassy state, based on the mobility of protein foci and lipid droplets. This transition occurs at the same pH in both populations but with completely different timing. This recapitulates the transition observed after abrupt starvation. It shows that the same transition occurs in viable, quiescent cells and provide further evidence that it is correlated with pH changes.
The only concern I have is that they used only one strain, which reduces the universality of their findings. Moreover, it is ambiguous which strain was used. The strain table says they used S288c which is known to carry a hap1 mutation that compromises respiration and isn't the best choice for studying respiring cells. The text mentions that they are working in the BY background, (where most of their GFP studies have been carried out. The BY strains have the same hap1 mutation and several other unknown polymorphisms that prevent ethanol utilization and biomass increase after the diauxic shift.
Reviewer #1 (Significance (Required)):
This kind of single cell analysis is clearly the way forward and will have many further applications to understanding how cells adapt to their environment. The paper is well written and the figures are well laid out and easy to understand. It is a significant advance for the field and will set the bar for future experiments. However, this work was done with a single strain that is known to be defective in respiration. It would be extremely valuable to know if their results with this strain are generalizable to other lab and wild strains.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
In this manuscript, the authors interrogated single cells of yeast as they developed into quiescence after the natural depletion of glucose from the culture medium. To do so, they constructed a microfluidic platform to track individual cells in a batch culture of cells transitioning from a growing phase into stationary phase. They then used a number of assays to monitor the metabolic changes that accompany this transition. They observed that internal pH dropped during development of quiescence, with some cells showing a rapid drop and others showing a delayed and heterogeneous drop. At diauxie, cells transition from fermentation to respiration, and the minority of cells that showed a rapid drop in pH were respiration-deficient (R-) and unable to resume growth, while cells with a delayed pH drop were respiration proficient (R+) and able to resume growth. Using established markers to follow the previously described structural changes that accompany the development of quiescence, they found that the pH changes were temporally related to these structural changes. They suggest that the dynamic changes in intracellular pH promote waves of structural remodeling that eventually leads to a transition of cells to a gel-like state. The early drop in pH in R- cells was proposed to lead to a precocious transition of the cytoplasm, contributing to the inability of these cells to resume growth.
This study is well done, well-written, and the results are clearly presented and generally convincing. Data accumulation and analysis were well documented and appropriate statistics were used. While the authors provided details of the materials used to construct the microfluidic device, it would be appropriate for them to provide a detailed blueprint (and a video, for example) to other investigators who would like to employ this device in their studies of quiescence once this manuscript has been published.
Reviewer #2 (Significance (Required)):
The cell fate program that is set in motion as yeast cells transition from fermentation to respiration is still not well understood. The development of the microfluidic platform described in this manuscript could make a significant contribution to our understanding of the succession of metabolic and structural changes occurring during this transition. The Sagot lab has made a series of important contributions in this area, and the application of single cell tracking to monitor the temporal program of these changes represents a major technical advance that will be of general interest to researchers interested in defining the developmental programs that contribute to cellular quiescence and longevity.
Expertise: yeast chromatin biology
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Referee #2
Evidence, reproducibility and clarity
In this manuscript, the authors interrogated single cells of yeast as they developed into quiescence after the natural depletion of glucose from the culture medium. To do so, they constructed a microfluidic platform to track individual cells in a batch culture of cells transitioning from a growing phase into stationary phase. They then used a number of assays to monitor the metabolic changes that accompany this transition. They observed that internal pH dropped during development of quiescence, with some cells showing a rapid drop and others showing a delayed and heterogeneous drop. At diauxie, cells transition from fermentation to respiration, and the minority of cells that showed a rapid drop in pH were respiration-deficient (R-) and unable to resume growth, while cells with a delayed pH drop were respiration proficient (R+) and able to resume growth. Using established markers to follow the previously described structural changes that accompany the development of quiescence, they found that the pH changes were temporally related to these structural changes. They suggest that the dynamic changes in intracellular pH promote waves of structural remodeling that eventually leads to a transition of cells to a gel-like state. The early drop in pH in R- cells was proposed to lead to a precocious transition of the cytoplasm, contributing to the inability of these cells to resume growth.
This study is well done, well-written, and the results are clearly presented and generally convincing. Data accumulation and analysis were well documented and appropriate statistics were used. While the authors provided details of the materials used to construct the microfluidic device, it would be appropriate for them to provide a detailed blueprint (and a video, for example) to other investigators who would like to employ this device in their studies of quiescence once this manuscript has been published.
Significance
The cell fate program that is set in motion as yeast cells transition from fermentation to respiration is still not well understood. The development of the microfluidic platform described in this manuscript could make a significant contribution to our understanding of the succession of metabolic and structural changes occurring during this transition. The Sagot lab has made a series of important contributions in this area, and the application of single cell tracking to monitor the temporal program of these changes represents a major technical advance that will be of general interest to researchers interested in defining the developmental programs that contribute to cellular quiescence and longevity.
Expertise: yeast chromatin biology
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Referee #1
Evidence, reproducibility and clarity
These investigators have teamed up to solve a technical problem that has thwarted efforts to get a clear picture of the chronology of events in yeast cultures as they naturally exhaust their nutrient supply. This is a challenge because the time course is long and the density of the culture makes single cell analysis problematic. Previous studies involving abrupt starvation have shown that there is a pH drop when nutrients are eliminated, but abrupt starvation also leads to rapid loss of viability compared to what is observed with cells as they respond and adapt to changes in their environment. This microfluidic devise and an intracellular pH detector allowed them to follow pH change as cells transition from fermentation to respiration and stationary phase. About 15% of the population responds completely differently than the other 85%, making this single cell analysis crucial. It also provides a negative control of sorts, to further substantiate the correlations they draw. This 15% fails to enter the respiratory phase and dies rapidly. The pH also drops rapidly and is correlated with loss of mitochondrial function and aggregation of proteins. The 85% of cells that succeed in shifting to respiration suffer the same pH drop, but it is much slower and is correlated with slower protein aggregation, P Body, actin body, and proteosome storage Granule assembly. They also followed the cytoplasmic transition to a glassy state, based on the mobility of protein foci and lipid droplets. This transition occurs at the same pH in both populations but with completely different timing. This recapitulates the transition observed after abrupt starvation. It shows that the same transition occurs in viable, quiescent cells and provide further evidence that it is correlated with pH changes.
The only concern I have is that they used only one strain, which reduces the universality of their findings. Moreover, it is ambiguous which strain was used. The strain table says they used S288c which is known to carry a hap1 mutation that compromises respiration and isn't the best choice for studying respiring cells. The text mentions that they are working in the BY background, (where most of their GFP studies have been carried out. The BY strains have the same hap1 mutation and several other unknown polymorphisms that prevent ethanol utilization and biomass increase after the diauxic shift.
Significance
This kind of single cell analysis is clearly the way forward and will have many further applications to understanding how cells adapt to their environment. The paper is well written and the figures are well laid out and easy to understand. It is a significant advance for the field and will set the bar for future experiments. However, this work was done with a single strain that is known to be defective in respiration. It would be extremely valuable to know if their results with this strain are generalizable to other lab and wild strains.
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Reply to the reviewers
Response/revision plan
(Point-by-point response)
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
The manuscript by Pennauer et al is the first to systematically investigate the role of class I&II Arfs using a knockout approach. It builds on earlier work by the Kahn lab who used an RNAi approach (Volpicelli-Daley et al. 2005) and is complementary to the overexpression approach used by the Hauri lab (Ben-Tekaya et al, 2010). The work is elegant and the data are strong. I am strongly in favor of publishing this work and my comments are technical in nature (2-5) and a request for some text changes (1). have the following comments for improvements:
1- When it comes to evaluating the role of depletions of Arfs on cell fitness, it would be better to use a non-transformed cell line. I am not asking the authors to go through the painstaking process of generating knockout cell lines in RPE1 cells for instance. Rather, I suggest that the authors make the reader aware that conclusions about cell survival have to be taken with care due to the use of a transformed cell line.
We will add this valid point to the Discussion.
2- Why do Arf1 and Arf4 ko cells grow more slowly. Is it a higher rate of cell death? Is it a block in a certain phase of the cell cycle. Given the link of the Golgi to G2-M entry, I think that an analysis of the cell cycle distribution would add more depth to these data. If the cell cycle distribution is unaffected, then I would conclude that that the difference in doubling time are due to reduced cell survival. If there is an effect on the cell cycle distribution, then the conclusion of the authors is safe that no single Arf is required for survival
We plan to analyze cell cycle distribution.
3- It is not clear to me how many cells were quantified in Figure 2D-F. I suppose that each dot represents a cell. In this case, the number of cells quantified is a bit low. Such a quantification of fluorescence intensities in two channels in the same region is a simple task and I think it should be no problem obtaining at least 100 cells per condition.
We will add the number of cells analyzed to the figure legends: At least 40 Golgis were quantified in each experiment. thus >100 in total.
4- Is the drop in the ratio of beta-COP/GM130 in Arf1 depleted cells reflecting reduced recruitment to the Golgi? Because the Golgi is bigger, it might be reflecting a reduced density in the number of coatomer molecules per surface area. If it is due to reduced recruitment, then the ratio of membrane/cytosolic betaCOP should be altered. This of course requires to show that the knockout does not affect total levels of coatomer. I think that such fractionation experiments would be a valuable addition to the manuscript and increase the depth of the data.
We are currently performing immunoblot analysis to determine bCOP levels.
In the Figure below, we have plotted the total intensity of GM130 or bCOP per Golgi from our immunoflurescence data. Total intensity of GM130 significantly increased in the cell lines lacking Arf1, consistent with the increase in Golgi volume. The amount of bCOP at the Golgi remained constant, resulting in reduced bCOP/GM130 ratio. Deletion of Arf1 thus results in reduced rate of coat recruitment that is compensated by an increase in Golgi mass. In the simplest model, reduced formation of Golgi-exit carriers causes Golgi growth until exit carrier formation allows for the required flux.
We propose to include this data in the revised manuscript.
FIGURE
5- The finding that Arf4-ko cells exhibit a defect on retrieval of ER-resident proteins is exciting, and in my opinion, it is the most significant finding in this manuscript. How can this be reconciled with the lack of an ARf4 ko effect on coatomer recruitment to the Golgi. Looking carefully at the data, I see that in 2 out of 3 experiments, Arf4 ko reduced the betaCOP/GM130 ratio. This is why I think it is crucial to perform more experiments and add more cells to increase the confidence in the data. Reduced retrieval of ER chaperones is frequently found in tumors and we still don't understand the reason behind this. Therefore, this finding is of significance beyond the community of cell biologists.
We plan to repeat quantitation with COPI for better statistical validity.
6- I find Figure 6A confusing. Why do Arf1 overexpressing parental HeLa cells exhibit less Arf1 than control cells?
In order not to overload the immunoblot of Arf overexpressing lysates, a smaller aliquot (1/20) was loaded. We will indicate this directly below the blots to make this more obvious in the revised figure.
7- Why was the following condition not tested: Arf4ko cells with Arf1 overexpression. Given the importance of Arf1 in retrograde (Golgi-to-ER) trafficking, I would expect a partial rescue of the retrieval of ER chaperones.
We will to do this experiment.
Reviewer #1 (Significance (Required)):
**Significance of the work:**
The paper is important because it is the first to examine the role of Arfs using a knockout approach. Another very important finding is that Arf4 depleted cells exhibit problems with retrieval of ER chaperones. This is a very novel finding and to the best of my knowledge
**Audience:**
The primary audience is of course the community working on membrane trafficking, organelle biology and proteostasis. However, I think that the data on the role of Arf4 in retrieval of ER chaperones might be of relevance for cancer biologists. Secretion of ER chaperones is frequently found in many tumors and we still do not understand why this is happening and what the significance thereof is.
**My own expertise:**
Export from the endoplasmic reticulum Golgi fragmentation in cancer cell migration Rho GTPases Kinase signaling Pseudoenzymes Cell migration of breast cancer cells Proteostasis in multiple myeloma
**Referee Cross-commenting**
Just a follow-up comment from my side:
I agree that it has not been unequivocally established that Arf1 is the main/sole of retrograde transport. However, even less established is the role of Arf4 in this process. The authors show that it is mainly Arf1 depletion that reduces the amount of COPI at the Golgi (ratio of COPI/GM130). Thus, I remain very surprised that it is actually the Arf4 depletion that results in reduced retrieval.
What is the significance of having less COPI at the Golgi in Arf1-ko cells? Certainly, the Golgi is not more "leaky". Does the level of COPI at the Golgi not reflect the strength of retrograde trafficking? Maybe there is no less COPI at the Golgi, and it only appears to be less, because the Golgi is bigger. This is why a simple fractionation experiment would be good. Something like making a cytosol and a microsome fraction and looking at the ratio of COPI (Cyt/Mem).
If both reviewers think it is too much, or unlikely to work, then I am happy to drop this point.
Below are my comments to the evaluations by the other two reviewers:
1- I agree with most comments that the two other reviewers made. Some of them are actually overlapping with mine (e.g. the use of a cell line other than HeLa).
2- I am not sure whether the impact of the paper would improve by adding data on Arf6.
3- To the comment on Golgi polarity. Maybe we could be more specific here and say that it would be sufficient to show that a trans-Golgi protein and a cis-Golgi protein can be separated by fluorescence microscopy, or whether we alternatively want them to actually do it by immunogold labeling for EM (which is more difficult).
4- I agree with reviewer 2 that the work proposed needs 1-3 months. I think reviewer 3 is a bit too optimistic with 1 month, because her/his comment on using a cell line other than HeLa cannot be addressed in just a month.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Pennauer uses HeLa cells and CRISPR/Cas9 to delete the 5 members of the class I and class II ARF family of small regulatory GTPases either individually or in combinations. The characterization of the KO cells is excellent and convincingly demonstrates that true KOs were generated. The quality of the data presented is high. Using the KO cells she documents minor alterations in Golgi architecture and the recruitment of vesicular coats in cells deleted of all ARFs except ARF4. In contrast, there is a significant lack of retention/recycling to the ER of KDEL-containing ER proteins in ARF4 KO cells, with numerous ER chaperones now released into the medium (the ARF4 KO secretome). This is a well-done study that showcases the ability of ARF4 alone to sustain cellular life (quite a surprise to this reviewer). Yet, the characterization of the phenotypes is somewhat minimal and the conclusions would be more robustly supported by additional experiments. Specifically:
- The authors completely ignore class III ARF6 and this paper would be much more comprehensive and informative if analysis of that ARF was also included (ARF6 has been seen at the Golgi and also mediates endosomal trafficking that intersects with the TGN).
In agreement with the reviewers' consensus in cross-commenting, we consider Arf6ko to be beyond the scope of this study.
Although the overall Golgi architecture seems to be largely conserved, it remains essential to test whether Golgi polarity is similarly maintained, and such data would significantly expand the significance of the reported findings
We have performed super-resolution microscopy of wild-type and Arf1ko Golgis for GM130 and TGN46 as cis- and trans-Golgi markers, respectively, showing that polarity is still intact for Arf1ko, the morphologically most affected knockout cell line. We plan to include the following Figure in the revised manuscript.
FIGURE
Golgi complexes were imaged by superresolution microscopy for GM130 (green) and TGN46 (red), and displayed as maximum intensity projections, or tomographic 2D slices. Scale bar, 3 μm.
Since there is a defect in retrieval of KDEL-proteins, it would be important to show the intracellular localization of the KDEL-R in the cells (especially in the ARF4 KO cells that don't retrieve KDEL-GFP) - is the receptor degraded, stuck in some specific place - knowing that would increase the impact of this study and provide a mechanistic explanation for the observed phenotype
We plan to perform immunoblot analysis for KDELR to test for changes in levels in Arf deletion cells, and immunofluorescence microscopy to analyze changes in KDELR localization.
The rescue experiments in Figure 6 are good as far as they go, but this experiment would be much more informative if in addition to the same class rescue, the other class ARFs (at least one!) were also characterized.
We will to do this experiment.
This is maybe a little too much to ask, but since the authors propose a mechanistic explanation for the ARF4 KO KDEL phenotype as being due to different effectors recruited by this ARF (in this case different COPI isotypes - this study would increase in impact by actually testing this mechanisms by assessing whether ARF4Q71L mutant preferentially bound any particular isotype of COPI or even try to do mass spec to identify relevant effectors for this extremely interesting ARF.
We also think that this additional analysis is beyond the scope of this study.
The Discussion is a very limited and would be more impactful by adding some discussion of organismal effects of ARF deletions (many are embryonic lethal while cells seems to live quite happily) or mutations (links to cancer come to mind here), as well as some mention of data from yeast ARF (what is and isn't essential in those cells). As is, the authors miss an opportunity to highlight the importance of their findings as they relate to current knowledge of ARFology.
We agree to add a discussion of information on embryonic lethality and disease.
Reviewer #2 (Significance (Required)):
This is an important paper for the ARF field and people interested in ARF signaling will be glad to read about the findings and perhaps also use the developed KO cell lines - this is a significant advancement. The impact would be even higher if some of the experiments suggested above were incorporated into the manuscript.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
This paper describes the application of CRISPR/Cas9 to systematically delete from HeLa cells all four Arf genes, either singly or in combination. The authors find it is possible to generate a number of double deletions (notably one lacking both Class I Arfs), and a triple deletion lacking all but Arf4. The authors characterise the structure of the Golgi in these mutants as well as retention of ER residents. The work is a comprehensive study of an exceptionally high technical standard. There is excellent validation of the deletions, and then the application of a wide range of methods including immunofluorescence, electron microscopy and mass-spectrometry, all with careful and extensive quantitation. The finding that cells can survive without Class I Arfs is interesting and unexpected, as is the fact that Arf4 alone is sufficient. This work will provide an excellent platform for future studies on Arf protein function in human cells. There are of course many questions that arise from these findings, but given the scope and quality of the work they would seem better left for future publications. There is one experiment that could be added, and some additions needed to the text for clarity and minor adjustments to the figures (all listed below), but if these are addressed, this would be a high quality paper of wide audience to a cell biological audience.
**Specific comments:**
1) Have the authors tested the levels and/or localisation of the KDEL receptor in the various lines? This is not essential, but if it were easily done, it would add to the work on ER resident secretion.
We plan to perform immunoblot analysis for KDELR to test for changes in levels in Arf deletion cells, and immunofluorescence microscopy to analyze changes in KDELR localization.
2) The work is entirely done in HeLa cells. The authors should note that the situation might be different in other cells types and cell lines. For instance, the DepMap CRISPR database suggests that quite a lot of cell lines are strongly affected by loss of Arf1.
We agree to add a discussion on known effects in other tissues.
3) Figure 2. Please show single channels as grey scale, and only merge as RGB. This is easier to see, especially for the colour blind. Likewise, Figure 3D would be clearer in greyscale rather than green, and 6B better in grey than in red.
We will make these changes.
4) Figure 5C. A brief comment is needed as to why it might be that BiP and calreticulin are not so efficiently secreted when Arf5 is knocked out in addition to Arf4.
This was a mistake in labeling that lane and will be corrected. It should read "Arf3+5ko" not "Arf4+5ko. Thank you for pointing this out.
5) Discussion:
a) The authors should relate these studies to work in other species. For instance, in yeast reduction of Arf levels causes the Golgi to enlarge (PubMed ID 9487133).
We can discuss this.
- b) Some more discussion is needed of the fact that Arfs may not all act in the same part of the Golgi, which could explain some of the differences observed between the various deletions.
We can add this point in the discussion.
Reviewer #3 (Significance (Required)):
The Arf GTPases have been studied extensively for over 30 years as major regulators of Golgi function. They are essential for the recruitment to Golgi membranes of both COPI and clathrin/AP-1 coats, as well as various other proteins that regulate Golgi function. In addition, they have been reported to have roles in viral replication, and even other cellular processes such as lipid droplet formation and mitochondrial division. In humans there are four Arfs, Arf1 and Arf3 (Class I Arfs), and Arf4 and Arf5 (Class II Arfs). All are present on the Golgi, but their precise individual roles have remained unclear. Attempts have been made to deplete individual Arfs using RNAi, but incomplete knockdowns have made the results hard to interpret.
**Referee Cross-commenting**
There is probably no need for a prolonged debate about this, but I agree that the importance of Arf4 is striking, but it reflects the nature of this work that CRISPR has finally allowed these sorts of questions to be addressed unequivocally. COPI is also involved in recycling of Golgi resident enzymes, and it may be that Arf1 acts in this role.
If the authors check levels of COPI by blotting, and measure the intensity over the Golgi by quantitative IMF, that will reveal whether stability or membrane association if affected without fractionation which is probably less reliable.
If they want to do some extra experiments, then it would be quite easy to check the levels of some Golgi enzymes, or look at lectin binding as a proxy for glycosylation enzyme levels.
Overall, I agree with the positive comments of Reviewers 1 and 2, and it good that we all recognise the quality and importance of the work. However, I feel that one or two of their requests go beyond the scope of a single publication, or would add rather little for a lot of additional work. It is of course easy to propose experiments that someone else has to do!
**[On] Reviewer 1:**
Point 4. I agree that it would be useful to perform a blot to determine if the levels of coatomer are effected in the various KO lines. I am not sure if Reviewer 1 is also proposing fractionation to determine cytosol vs membrane ratio, but if so, then this would be less useful as peripheral membrane proteins tend to fall off membranes during fractionation and so such analysis is generally questionable. A blot, and clarification of the way the COPI/GM130 ratio is determined, would answer the key points in a relatively straightforward way.
Point 5. I agree that the defect in retrieval of ER residents in Arf4-KO is striking, but it a clear effect even if the reviewer does not understand it themselves! It does not seem so surprising to me, given that Arf4 is likely to act on the early Golgi were such retrieval occurs from. However, the experiment suggested by myself and Reviewer 32 of checking the levels and localisation of the KDEL-receptor would seem to me a good first step to addressing possible mechanism, and certainly sufficient for an initial publication.
Point 7. I am not sure that it has been unequivocally established that Arf1 is important in retrograde traffic. The reality is that many labs have taken Arf1 as being representative of all others and so concentrated biochemical and in vivo studies on this protein. This paper is really important as it highlights the need to investigate both Class I and Class II Arfs, and to bear in mind that their roles in vivo may well be more distinct than their in vitro properties would lead one to suspect. Perhaps, the simplest explanation for this is that the GEFs that activate them have a strong preference for one or the other.
Follow up Comment 1. I was not suggesting that the authors repeat all this in a cell line other than HeLa cells, as this is clearly impractical. HeLa cells are widely used, and so the findings are useful, and whilst it seems certain that some other cell lines would give different data (and indeed the DepMap data show this), then testing one other line would not change the conclusions much. All I wanted the authors to do is to clearly state in the text that what they see in HeLa cells may well be different in other cell lines. This does not detract from the fact that their HeLa cells will provide an excellent platform for focused studies on the role of individual Arfs.
Follow up Comment 2. I agree that Arf6 is not relevant to this paper (as discussed in detail below).
Follow up Comment 3. agree that a simple IMF experiment would suffice to check polarity and immuno-EM is technically very demanding and would add little in this context. The authors have already shown that the Golgi forms stacks in the KO cell lines, and I cannot see how this could occur without the stack being polarised - it has to form at one end and then mature to the other. In addition, after decades of working on the Golgi I have yet to see a credible report of a change to cells causing a loss of Golgi polarity, but maintaining a stacked structure. If the Golgi is not polarised it could not form a stack.
Follow up Comment 4. I agree that one month is perhaps too short to look at KDEL-R, COPI levels and checking polarity by IMF. As noted above, I am NOT suggesting that they repeat all this in a different cell line.
**[On] Reviewer 2.**
Point 1. I agree with Reviewer 1 that the authors are correct to ignore Arf6. It is a completely different GTPase with a distinct function in a different part of the cell. The family of Arf1-Arf5 arose in metazoans from a single Arf, but Arf6 had already split away from the Arf1-5 family in the last eukaryotic common ancestor, as Arf6 is present in plants and yeasts. There is overwhelming evidence that Arf1-Arf5 are partially redundant and this has hampered their study. Arf6 does not share these roles. The fact that it is acts on endosomes and has been reported to be on the Golgi (which is not widely agreed), is also true of many other GTPases. Indeed, other distant relatives of Arf1-5 are actually on the Golgi (Arl1, Arl5 etc), but these are also not relevant as like Arf6 they do not bind coat proteins and other major effectors of Arf1-5.
Point 2. As noted above, it is hard to see how polarity could be affected given that a Golgi stack is formed, but, at most, a simple application of IMF would seem sufficient to confirm this.
Point 3. Agreed.
Point 5. I agree with the reviewer that this is (much!) too much to ask for an initial publication. Various labs have already reported analysis of the effectors of Class II Arfs and they tend to overlap with Class I. Moreover, it is quite possible that the difference of role in vivo reflects differing interactions with regulators.
Point 6. Agreed.
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Referee #3
Evidence, reproducibility and clarity
This paper describes the application of CRISPR/Cas9 to systematically delete from HeLa cells all four Arf genes, either singly or in combination. The authors find it is possible to generate a number of double deletions (notably one lacking both Class I Arfs), and a triple deletion lacking all but Arf4. The authors characterise the structure of the Golgi in these mutants as well as retention of ER residents. The work is a comprehensive study of an exceptionally high technical standard. There is excellent validation of the deletions, and then the application of a wide range of methods including immunofluorescence, electron microscopy and mass-spectrometry, all with careful and extensive quantitation. The finding that cells can survive without Class I Arfs is interesting and unexpected, as is the fact that Arf4 alone is sufficient. This work will provide an excellent platform for future studies on Arf protein function in human cells. There are of course many questions that arise from these findings, but given the scope and quality of the work they would seem better left for future publications. There is one experiment that could be added, and some additions needed to the text for clarity and minor adjustments to the figures (all listed below), but if these are addressed, this would be a high quality paper of wide audience to a cell biological audience.
Specific comments:
1) Have the authors tested the levels and/or localisation of the KDEL receptor in the various lines? This is not essential, but if it were easily done, it would add to the work on ER resident secretion.
2) The work is entirely done in HeLa cells. The authors should note that the situation might be different in other cells types and cell lines. For instance, the DepMap CRISPR database suggests that quite a lot of cell lines are strongly affected by loss of Arf1.
3) Figure 2. Please show single channels as grey scale, and only merge as RGB. This is easier to see, especially for the colour blind. Likewise, Figure 3D would be clearer in greyscale rather than green, and 6B better in grey than in red.
4) Figure 5C. A brief comment is needed as to why it might be that BiP and calreticulin are not so efficiently secreted when Arf5 is knocked out in addition to Arf4.
5) Discussion:
a) The authors should relate these studies to work in other species. For instance, in yeast reduction of Arf levels causes the Golgi to enlarge (PubMed ID 9487133).
b) Some more discussion is needed of the fact that Arfs may not all act in the same part of the Golgi, which could explain some of the differences observed between the various deletions.
Significance
The Arf GTPases have been studied extensively for over 30 years as major regulators of Golgi function. They are essential for the recruitment to Golgi membranes of both COPI and clathrin/AP-1 coats, as well as various other proteins that regulate Golgi function. In addition, they have been reported to have roles in viral replication, and even other cellular processes such as lipid droplet formation and mitochondrial division. In humans there are four Arfs, Arf1 and Arf3 (Class I Arfs), and Arf4 and Arf5 (Class II Arfs). All are present on the Golgi, but their precise individual roles have remained unclear. Attempts have been made to deplete individual Arfs using RNAi, but incomplete knockdowns have made the results hard to interpret.
Referee Cross-commenting
There is probably no need for a prolonged debate about this, but I agree that the importance of Arf4 is striking, but it reflects the nature of this work that CRISPR has finally allowed these sorts of questions to be addressed unequivocally. COPI is also involved in recycling of Golgi resident enzymes, and it may be that Arf1 acts in this role.
If the authors check levels of COPI by blotting, and measure the intensity over the Golgi by quantitative IMF, that will reveal whether stability or membrane association if affected without fractionation which is probably less reliable.
If they want to do some extra experiments, then it would be quite easy to check the levels of some Golgi enzymes, or look at lectin binding as a proxy for glycosylation enzyme levels.
Overall, I agree with the positive comments of Reviewers 1 and 2, and it good that we all recognise the quality and importance of the work. However, I feel that one or two of their requests go beyond the scope of a single publication, or would add rather little for a lot of additional work. It is of course easy to propose experiments that someone else has to do!
Reviewer 1:
Point 4. I agree that it would be useful to perform a blot to determine if the levels of coatomer are effected in the various KO lines. I am not sure if Reviewer 1 is also proposing fractionation to determine cytosol vs membrane ratio, but if so, then this would be less useful as peripheral membrane proteins tend to fall off membranes during fractionation and so such analysis is generally questionable. A blot, and clarification of the way the COPI/GM130 ratio is determined, would answer the key points in a relatively straightforward way.
Point 5. I agree that the defect in retrieval of ER residents in Arf4-KO is striking, but it a clear effect even if the reviewer does not understand it themselves! It does not seem so surprising to me, given that Arf4 is likely to act on the early Golgi were such retrieval occurs from. However, the experiment suggested by myself and Reviewer 3 of checking the levels and localisation of the KDEL-receptor would seem to me a good first step to addressing possible mechanism, and certainly sufficient for an initial publication.
Point 7. I am not sure that it has been unequivocally established that Arf1 is important in retrograde traffic. The reality is that many labs have taken Arf1 as being representative of all others and so concentrated biochemical and in vivo studies on this protein. This paper is really important as it highlights the need to investigate both Class I and Class II Arfs, and to bear in mind that their roles in vivo may well be more distinct than their in vitro properties would lead one to suspect. Perhaps, the simplest explanation for this is that the GEFs that activate them have a strong preference for one or the other.
Follow up Comment 1. I was not suggesting that the authors repeat all this in a cell line other than HeLa cells, as this is clearly impractical. HeLa cells are widely used, and so the findings are useful, and whilst it seems certain that some other cell lines would give different data (and indeed the DepMap data show this), then testing one other line would not change the conclusions much. All I wanted the authors to do is to clearly state in the text that what they see in HeLa cells may well be different in other cell lines. This does not detract from the fact that their HeLa cells will provide an excellent platform for focused studies on the role of individual Arfs.
Follow up Comment 2. I agree that Arf6 is not relevant to this paper (as discussed in detail below).
Follow up Comment 3. agree that a simple IMF experiment would suffice to check polarity and immuno-EM is technically very demanding and would add little in this context. The authors have already shown that the Golgi forms stacks in the KO cell lines, and I cannot see how this could occur without the stack being polarised - it has to form at one end and then mature to the other. In addition, after decades of working on the Golgi I have yet to see a credible report of a change to cells causing a loss of Golgi polarity, but maintaining a stacked structure. If the Golgi is not polarised it could not form a stack.
Follow up Comment 4. I agree that one month is perhaps too short to look at KDEL-R, COPI levels and checking polarity by IMF. As noted above, I am NOT suggesting that they repeat all this in a different cell line.
Reviewer 2.
Point 1. I agree with Reviewer 1 that the authors are correct to ignore Arf6. It is a completely different GTPase with a distinct function in a different part of the cell. The family of Arf1-Arf5 arose in metazoans from a single Arf, but Arf6 had already split away from the Arf1-5 family in the last eukaryotic common ancestor, as Arf6 is present in plants and yeasts. There is overwhelming evidence that Arf1-Arf5 are partially redundant and this has hampered their study. Arf6 does not share these roles. The fact that it is acts on endosomes and has been reported to be on the Golgi (which is not widely agreed), is also true of many other GTPases. Indeed, other distant relatives of Arf1-5 are actually on the Golgi (Arl1, Arl5 etc), but these are also not relevant as like Arf6 they do not bind coat proteins and other major effectors of Arf1-5.
Point 2. As noted above, it is hard to see how polarity could be affected given that a Golgi stack is formed, but, at most, a simple application of IMF would seem sufficient to confirm this.
Point 3. Agreed.
Point 5. I agree with the reviewer that this is (much!) too much to ask for an initial publication. Various labs have already reported analysis of the effectors of Class II Arfs and they tend to overlap with Class I. Moreover, it is quite possible that the difference of role in vivo reflects differing interactions with regulators.
Point 6. Agreed.
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Referee #2
Evidence, reproducibility and clarity
Pennauer uses HeLa cells and CRISPR/Cas9 to delete the 5 members of the class I and class II ARF family of small regulatory GTPases either individually or in combinations. The characterization of the KO cells is excellent and convincingly demonstrates that true KOs were generated. The quality of the data presented is high. Using the KO cells she documents minor alterations in Golgi architecture and the recruitment of vesicular coats in cells deleted of all ARFs except ARF4. In contrast, there is a significant lack of retention/recycling to the ER of KDEL-containing ER proteins in ARF4 KO cells, with numerous ER chaperones now released into the medium (the ARF4 KO secretome). This is a well-done study that showcases the ability of ARF4 alone to sustain cellular life (quite a surprise to this reviewer). Yet, the characterization of the phenotypes is somewhat minimal and the conclusions would be more robustly supported by additional experiments. Specifically:
- The authors completely ignore class III ARF6 and this paper would be much more comprehensive and informative if analysis of that ARF was also included (ARF6 has been seen at the Golgi and also mediates endosomal trafficking that intersects with the TGN).
- Although the overall Golgi architecture seems to be largely conserved, it remains essential to test whether Golgi polarity is similarly maintained, and such data would significantly expand the significance of the reported findings
- Since there is a defect in retrieval of KDEL-proteins, it would be important to show the intracellular localization of the KDEL-R in the cells (especially in the ARF4 KO cells that don't retrieve KDEL-GFP) - is the receptor degraded, stuck in some specific place - knowing that would increase the impact of this study and provide a mechanistic explanation for the observed phenotype
- The rescue experiments in Figure 6 are good as far as they go, but this experiment would be much more informative if in addition to the same class rescue, the other class ARFs (at least one!) were also characterized.
- This is maybe a little too much to ask, but since the authors propose a mechanistic explanation for the ARF4 KO KDEL phenotype as being due to different effectors recruited by this ARF (in this case different COPI isotypes - this study would increase in impact by actually testing this mechanisms by assessing whether ARF4Q71L mutant preferentially bound any particular isotype of COPI or even try to do mass spec to identify relevant effectors for this extremely interesting ARF.
- The Discussion is a very limited and would be more impactful by adding some discussion of organismal effects of ARF deletions (many are embryonic lethal while cells seems to live quite happily) or mutations (links to cancer come to mind here), as well as some mention of data from yeast ARF (what is and isn't essential in those cells). As is, the authors miss an opportunity to highlight the importance of their findings as they relate to current knowledge of ARFology.
Significance
This is an important paper for the ARF field and people interested in ARF signaling will be glad to read about the findings and perhaps also use the developed KO cell lines - this is a significant advancement. The impact would be even higher if some of the experiments suggested above were incorporated into the manuscript.
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Referee #1
Evidence, reproducibility and clarity
The manuscript by Pennauer et al is the first to systematically investigate the role of class I&II Arfs using a knockout approach. It builds on earlier work by the Kahn lab who used an RNAi approach (Volpicelli-Daley et al. 2005) and is complementary to the overexpression approach used by the Hauri lab (Ben-Tekaya et al, 2010). The work is elegant and the data are strong. I am strongly in favor of publishing this work and my comments are technical in nature (2-5) and a request for some text changes (1). have the following comments for improvements:
1- When it comes to evaluating the role of depletions of Arfs on cell fitness, it would be better to use a non-transformed cell line. I am not asking the authors to go through the painstaking process of generating knockout cell lines in RPE1 cells for instance. Rather, I suggest that the authors make the reader aware that conclusions about cell survival have to be taken with care due to the use of a transformed cell line.
2- Why do Arf1 and Arf4 ko cells grow more slowly. Is it a higher rate of cell death? Is it a block in a certain phase of the cell cycle. Given the link of the Golgi to G2-M entry, I think that an analysis of the cell cycle distribution would add more depth to these data. If the cell cycle distribution is unaffected, then I would conclude that that the difference in doubling time are due to reduced cell survival. If there is an effect on the cell cycle distribution, then the conclusion of the authors is safe that no single Arf is required for survival
3- It is not clear to me how many cells were quantified in Figure 2D-F. I suppose that each do represents a cell. In this case, the number of cells quantified is a bit low. Such a quantification of fluorescence intensities in two channels in the same region is a simple task and I think it should be no problem obtaining at least 100 cells per condition.
4- Is the drop in the ratio of beta-COP/GM130 in Arf1 depleted cells reflecting reduced recruitment to the Golgi? Because the Golgi is bigger, it might be reflecting a reduced density in the number of coatomer molecules per surface area. If it is due to reduced recruitment, then the ratio of membrane/cytosolic betaCOP should be altered. This of course requires to show that the knockout does not affect total levels of coatomer. I think that such fractionation experiments would be a valuable addition to the manuscript and increase the depth of the data.
5- The finding that Arf4-ko cells exhibit a defect on retrieval of ER-resident proteins is exciting, and in my opinion, it is the most significant finding in this manuscript. How can this be reconciled with the lack of an ARf4 ko effect on coatomer recruitment to the Golgi. Looking carefully at the data, I see that in 2 out of 3 experiments, Arf4 ko reduced the betaCOP/GM130 ratio. This is why I think it is crucial to perform more experiments and add more cells to increase the confidence in the data. Reduced retrieval of ER chaperones is frequently found in tumors and we still don't understand the reason behind this. Therefore, this finding is of significance beyond the community of cell biologists.
6- I find Figure 6A confusing. Why do Arf1 overexpressing parental HeLa cells exhibit less Arf1 than control cells?
7- Why was the following condition not tested: Arf4ko cells with Arf1 overexpression. Given the importance of Arf1 in retrograde (Golgi-to-ER) trafficking, I would expect a partial rescue of the retrieval of ER chaperones.
Significance
Significance of the work:
The paper is important because it is the first to examine the role of Arfs using a knockout approach. Another very important finding is that Arf4 depleted cells exhibit problems with retrieval of ER chaperones. This is a very novel finding and to the best of my knowledge
Audience:
The primary audience is of course the community working on membrane trafficking, organelle biology and proteostasis. However, I think that the data on the role of Arf4 in retrieval of ER chaperones might be of relevance for cancer biologists. Secretion of ER chaperones is frequently found in many tumors and we still do not understand why this is happening and what the significance thereof is.
My own expertise:
Export from the endoplasmic reticulum Golgi fragmentation in cancer cell migration Rho GTPases Kinase signaling Pseudoenzymes Cell migration of breast cancer cells Proteostasis in multiple myeloma
Referee Cross-commenting
Just a follow-up comment from my side:
I agree that it has not been unequivocally established that Arf1 is the main/sole of retrograde transport. However, even less established is the role of Arf4 in this process. The authors show that it is mainly Arf1 depletion that reduces the amount of COPI at the Golgi (ratio of COPI/GM130). Thus, I remain very surprised that it is actually the Arf4 depletion that results in reduced retrieval.
What is the significance of having less COPI at the Golgi in Arf1-ko cells? Certainly, the Golgi is not more "leaky". Does the level of COPI at the Golgi not reflect the strength of retrograde trafficking? Maybe there is no less COPI at the Golgi, and it only appears to be less, because the Golgi is bigger. This is why a simple fractionation experiment would be good. Something like making a cytosol and a microsome fraction and looking at the ratio of COPI (Cyt/Mem).
If both reviewers think it is too much, or unlikely to work, then I am happy to drop this point.
Below are my comments to the evaluations by the other two reviewers:
1- I agree with most comments that the two other reviewers made. Some of them are actually overlapping with mine (e.g. the use of a cell line other than HeLa).
2- I am not sure whether the impact of the paper would improve by adding data on Arf6.
3- To the comment on Golgi polarity. Maybe we could be more specific here and say that it would be sufficient to show that a trans-Golgi protein and a cis-Golgi protein can be separated by fluorescence microscopy, or whether we alternatively want them to actually do it by immunogold labeling for EM (which is more difficult).
4- I agree with reviewer 2 that the work proposed needs 1-3 months. I think reviewer 3 is a bit too optimistic with 1 month, because her/his comment on using a cell line other than HeLa cannot be addressed in just a month.
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity (Required)): **Summary:** In this study authors investigated the role of NAMPT, NAD+ and PARP1/parthanatos in skin inflammation using a zebrafish psoriasis model with an hypomorphic mutation of spint1a and human organotypic 3D skin models of psoriasis. Authors showed that genetic deletion and/or pharmacological inhibition of Nampt/PARP1/AIFM1/NADPH oxidases reduced oxidative stress, inflammation, keratinocyte DNA damage, hyperproliferation and cell death in zebrafish models of chronic skin inflammation. Authors also showed the expression of pathology-associated genes in human organotypic 3D skin models of psoriasis with pharmacological inhibition of Nampt/PARP1/AIFM1/NADPH oxidases. The key finding of this study is that PARP1 hyperactivation caused by ROS-induced DNA damage mediates skin inflammation through parthanatos. **Major comments:** This is a very comprehensive study to investigate the role of PARP1 in skin inflammation. The main conclusion was made based on the genetic inhibition and/or pharmacological inhibition of Nampt/PARP1/AIFM1/NADPH oxidases. Although the finding of this study that NAMPT-derived NAD+ fuels PARP1 to promote skin inflammation through parthanatos is interesting and important, there are lots of major concerns and questions, which have to be addressed to better support the main conclusion. In addition, the data and methods were not presented with sufficient detail.
- This study is heavily relied on pharmacology inhibition. However, the specificity and selectivity of many inhibitors were not tested in this study.
At least 3 concentrations of each inhibitor were tested and the lowest one able to rescue the phenotype was then used for further testing (please, see Table S1). More importantly, the specificity of all compounds used were confirmed by genetic inhibition of their targets.
Fig. 1: it is quite confusing how NAD+ increases H2O2 levels? Is NAD+ cell permeable? It is not clear if NAD+ has been really up taken by cells in the larvae. If NAD+ fuels PARP1 to promote skin inflammation, why NAM treatment increased H2O2 levels but NMN precursor failed to increase skin oxidative stress? No reasonable explanation has been provided.
This is an interesting point. We have shown that exogenous NAD+ added in the water of larvae increased larval NAD+ (please, see Fig. 2K). It has been shown that neurons can take up NAD+ through CX43 (Fig. S7), so a similar mechanism may operate in larval skin. As regards, the effect of NAM and NMN, a recent study has demonstrated that NAM supplementation increased zebrafish larval NAD+; however, NA, NMN and NR failed to boost larval NAD+ level (PMID: 32197067). These results are consistent with our data.
Fig. 1E and 1G: it is not clear what is the green channel. Similarly, there is no clear description what is red or green in many other figures.
To help the interpretation of larval pictures, we have indicated in all figures what is analyzed in each fluorescent channel.
- Fig. 1K and 1L: It is hard to understand why FK-866 reduced H2O2 release, but it increased neutrophils infiltration. How to interpret this conclusion?
Fig. 2C-D: Why low doses FK-866 reduced neutrophil infiltration whereas high dose FK-866 increased neutrophil infiltration?
Answer to 4&5: As it was explained in lines 145-156, FK-866 induces NF-kB activation in the muscle and neutrophil infiltration in this tissue when used at 100 uM. This result may be deleted if the reviewers think it is confusing, since a 10 uM dose was used in all subsequent experiments to study the impact of Nampt in skin inflammation. This dose has no effects in the muscle but robustly reduced skin H2O2 production and neutrophil skin infiltration.
Fig. 2I-J: it is not clear how NF-kB activity was measured. Is that based on green fluorescence shown in Fig. 2J? if so, the representative images were not consistent with the quantification data shown in I. Similarly, many other representative images were also not consistent with their quantification data throughout the manuscript. For example, Fig. 3C/D, 3E/F, 3G/H, 3L/M, Figure S2C/D, S2G/H, Fig. 4C/D, 4J/K.
The quantification of NFkB was measured in the skin, as it has already been reported previously (Candel et al., 2014). This is indicated in M&M section. The images show the whole larvae and NFkB is expressed at high levels in different tissues, such as neuromasts. To clarify this, we have included an additional figure to explain the ROI used for quantification of H2O2 and NfkB (Fig. S1G).
Figure S1C, Nampta/Namptb protein expression should be checked and shown after its KO using crispr/cas9 technique.
Unfortunately, we have used to different antibodies and both failed to crossreact with zebrafish Nampta/b. However, we have included the efficiency of CRISPR-Cas9 in Fig. S1F of the revised version. The efficiency is relatively low, probably indicating that is indispensable for zebrafish development, as occurs in mice (PMID 28333140).
Fig. 3I: protein expression of nox1, nox4 and nox 5 should be checked after genetic inhibition using CRISPR/Cas9 technique.
Unfortunately, we do not have antibodies able to recognize zebrafish Nox1, Nox4 and Nox5. However, we have provided the efficiency of the gRNA used for each gene (Fig. S3) and it is about 65%.
Fig. 4: If Olaparib treatment increased DNA damage, will it increase PARP1 activation and PAR formation?
As it has widely used in mammalian models, parthanatos is triggered by overactivation of PARP1 following DNA damage. Therefore, although inhibition of olaparib may further induces DNA damage, it blocks parthanatos. This is consistent with our results showing that olaparib reduces PARylation (Fig. S4H) and cell death (Figs. 4J, 4K).
Fig. 4M: it is not clear what staining has been done. No difference was observed among different groups.
As indicated in the figure legends, pγH2Ax+ (green) keratinocytes (red) are shown. We have indicated this in the figure and include arrows to show pγH2Ax+ cells. The quantitation of this experiment (Fig. 4L) show that FK-866 robustly reduced, while olaparib increases, keratinocyte DNA damage.
Authors used N-phenylmaleimide (NP) to block AIF nuclear translocation. How does this inhibitor work? what is its actual effect on AIF nuclear translocation? Experiments are required to show this inhibitor actually blocks AIF nuclear translocation.
NP has been shown to block AIFM1 nuclear translocation, since it inhibits cysteine proteases which are required for its cleavage which precedes nuclear translocation (PMID 8879205). Although we have shown that genetic inhibition of Aifm1 rescues skin inflammation, confirming the specificity of the inhibitor, we agree on this point. Therefore, we have performed additional experiments and showed nuclear Aifm1 in keratinocyte aggregates of Spint1-deficient larvae and that NP treatment blocked nuclear translocation (Fig. S6C). In addition, we have also shown increased nuclear translocation of AIFM1 in keratinocytes of lesional skin from psoriasis patients (Figs. 6C, 6D).
Figure S4: it is hard to understand why lane #2 with Olaparib has the highest PAR signal.
We are sorry for this mistake labeling the WB. The right legend is: 1 +/+, 2 -/- treated with DMSO, 3 -/- treated with FK-866 and 4 -/- treated with olaparib.
Does spint1a-/- zebrafish show parthanatos cell death? It is not clear how cell death was measured.
We have shown that skin keratinocytes from Spint1a-deficient fish show increased cell death, as assayed by TUNEL, that is fully reversed by olaparib (Figs. 4J, 4K). In addition, skin keratinocytes from the mutant fish also have increased PARylation that is reversed by either FK-866 or olaparib (Fig. S4G, S4H). Further, pharmacological and genetic inhibition of Aifm1 inhibition and forced expression of Parga also rescue skin inflammation. Finally, we have included new experiments showing Aifm1 nuclear translocation in both Spint1a-deficient larvae and psoriasis patient lesional skin. Therefore, all these results show that Spint1a-deficient fish show parthanatos cell death-induced inflammation.
NAD+ levels were regulated by 3 different pathways. Expression of many genes involved in these 3 pathways were altered in psoriasis. However, it is not clear if the other two pathways play a role in PARP1-mediated inflammation.
NAD+ salvage pathway has been shown to be the major pathway regulating NAD+ levels in most tissues. The inhibition of this pathway with FK-866 rescues all skin phenotypes observed in Spint1a-deficient larvae as well as in organotypic 3D skin models of psoriasis. These results were further validated using another inhibitor (GMX1778) and genetic inhibition. Therefore, our results support that the salvage pathway is the one involved in psoriasis and inhibition of this pathway would rescue inflammation. However, it will be worthy to investigate if other pathways play a role in psoriasis and specifically upon inhibition of the salvage pathway.
**Minor comments:**
- Page 9: To test this hypothesis, we used N-phenylmaleimide (NP), a chemical inhibitor of Aifm1 translocation from the nucleus to the mitochondria (Susin et al., 1996). The statement is not correct.
We are sorry for this mistake. It has been amended to: “To test this hypothesis, we used N-phenylmaleimide (NP), a chemical inhibitor of Aifm1 translocation from the mitochondria to the nucleus (Susin et al., 1996).”
Page 12: To the best of our knowledge, this is the first study demonstrating the existence of parthanatos in vivo. This statement is not correct.
We have removed this statement.
Figure S3 and S6E: they should be presented in an easy understandable way for the general readers.
We have explained in the legends the graph output of TIDE analysis.
Figure legends should be presented in a clearer way.
We have tried our best writing the legends. All suggestions and request were made.
Reviewer #1 (Significance (Required)): Parthanatos is a new type of cell death distinct from apoptosis, necrosis, necroptosis and plays a pivotal role in ischemic stroke and neurodegenerative diseases (Wang Y et a., Science. 2016; Kam TI et al., Science 2018). The current study may provide new evidence of the importance of PARP1 and parthanatos in skin inflammation and potential targets for the treatment of skin inflammation. We thank the reviewer’s opinion on the significance of our study.
The reviewer has the expertise in oxidative stress, PARP1 and parthanatos research. Reviewer #2 (Evidence, reproducibility and clarity (Required)): **Summary:** The manuscript entitle "NAMPT-derived NAD+ fuels PARP1 to promote skin inflammation through parthanatos" is well written, divided and organized. This work demonstrated that models of psoriasis are characterized by ROS stress, inflammation and cell death. It was clear that NAMPT, a rate-limiting enzyme of NAD salvage pathway, and PARP1, a Poly-ADP-ribose polymerase, could be targeted to decrease ROS stress and inflammation that are contributing to cell death through parthanatos pathway. However, it was not clear that NAD+ are the responsible for fuel these processes in the psoriasis models analyzed. Nevertheless, the present work demonstrated that the cell death observed in the psoriasis model analyzed was correlated to an unidentified programmed cell death pathway, parthanatos that up to date has not been demonstrated.
We are pleased with the reviewer’s comments on our study.
**Major comments:** Most of the data showed confirmed that inhibition of NAMPT or PARP1 seems to be beneficial for the relief of some characteristics related to oxidative stress and inflammation in the skin. However, the author should show data about NAD+ levels only instead of the ratio NAD+/NADH to state that NAMPT-derived NAD+ is promoting oxidative stress (line 366-368) (fig2K).
The data shown in Fig 2K are NAD+ plus NADH. Considering that cytosolic and nuclear NAD+/NADH ratio typically ranges from 100 to 1000 (PMID: 21982715), these data mainly show intracellular NAD+ concentration in larvae.
Some data images are not convincing, or they don't really show an increase or decrease as the author showed in graph data. (Fig1D, 1E - 1F,1G).
The quantification of H2O2 and NFkB was measured in the skin, as it has already been reported previously (Candel et al., 2014). To clarify this, we have shown the ROI used for quantification of H2O2 and NfkB in Fig. S1G.
What is the relevance to analyze muscle and what is the relevance of the results obtained, since the effect of FK-866 in muscle increases the NFKB activity?
This is essentially a similar concern raised by reviewer 1. FK-866 induces NF-kB activation in the muscle and neutrophil infiltration in this tissue when used at 100 uM. This result may be deleted if the reviewers think it is confusing, since a 10 uM dose was used in all subsequent experiments to study the impact of Nampt in skin inflammation. This dose has no effects in the muscle but robustly reduced skin H2O2 production and neutrophil infiltration.
Figure S4H is not convincing with what the author wrote.
We are sorry for this mistake labeling the WB. The right legend is: 1 +/+, 2 -/- treated with DMSO, 3 -/- treated with FK-866 and 4 -/- treated with olaparib. Both FK-866 and olaparib rescue PARylation in the skin of Spint1a-deficient larvae.
The author should make the keratinocyte aggregation experiment with FK-866 treatment to better substantiate what they are proposing.
These results are shown in Figs. 2E and 2F.
**Minor comments:** Line 281: "NP, a chemical inhibitor of Aifm1 translocation from the nucleus to the mitochondria..." should be the opposite: NP, a chemical inhibitor of Aifm1 translocation from mitochondria to nucleus.
We are sorry for this mistake. It has been amended.
Line 299 "figure 6A" should be Figure 6B.
We have checked and it is correct.
How the author explains the relationship between all the results being related to NAMPT and supposedly to NAD+, but an important precursor to make NAD through salvage pathway (NMN) and a well NAD+ booster didn't show any effect?
This is an interesting point that was also raised by reviewer 1. A recent study has demonstrated that NAM supplementation increased zebrafish larval NAD+; however, NA, NMN and NR failed to boost larval NAD+ level (PMID: 32197067). This explains our results. We have discussed this point in the revised manuscript.
Line 178: should be NAMPT inhibitor stead of FK-866 inhibitor.
Thanks a lot. It has been amended.
Line 191-192: I suggest reformulating this sentence since the result showed was only the ratio NAD/NADH.
Please, see our response above. We are measuring NAD+ plus NADH. We have amended the text to clarify this fact.
Reviewer #2 (Significance (Required)): The present work greatly demonstrated the relevance of PARP1 and NAMPT in the field of inflammation and ROS in the skin that contribute to diseases like psoriasis. Although it is not a lethal disease, as the author mentioned, it affects the physical and mental health of the individual. Understanding the mechanism that underlie this condition would help to trigger new and more efficient treatments. It was clear that the result showed a promising strategy in targeting NAMPT and PARP1. Furthermore, inhibitor for them is already know and may be useful for future treatment of psoriasis disease. We thank this comments on the impact of our study.
Reviewer #3 (Evidence, reproducibility and clarity (Required)): This study shows NAMPT derived NAD facilitates PARP activation to promote skin inflammation via parthanatos. The authors used the zebrafish model and organoid models of psoriasis and observed that inhibition of NAMPT reduces inflammation in zebrafish and human skin organoid models. They also observed that NADPH oxidase-derived oxidative stress activates PARP, and PARP inhibition or over-expression of PARG or AIF mimics protection mediated by NAMPT inhibition. This is an interesting study, but there are several weaknesses to support the conclusions of this study. While pharmacological inhibition is a powerful tool, complementary methods (knock out of PARP-1) are critical for this paper's conclusions. PARP inhibitor used in this study may not specifically inhibit PARP1 but other PARPs too. Therefore, genetic knockout of PARP will make the make this conclusions/interpretation of this study strong.
We thank these comments on our manuscript. All pharmacological inhibitions used in this study were confirmed by genetic experiments, including Parp1. The genetic inhibition of Parp1 is shown in Figs. S4C-S4F.
Additional comments include: This study's primary focus is PARP activation and PAR-mediated parthanatos, but it is not shown how different inhibitors used in this study and supplementations of NAD alter PARP activation and PAR formation.
We have shown through the quantitation of PARylation that Spint1a-deficient skin shows increased PAR activity and that pharmacological inhibition of either Nampt or Parp was able to fully reverse it (Figs S4g & S4H). In addition, we have also shown a dramatically increased PAR activity in lesional skin biopsies from psoriasis patients (Fig. 6E).
NAMPT is not the only NAD biosynthesis pathway; how other NAD pathways respond when NAMPT is inhibited with FK-866.
NAD+ salvage pathway has been shown to be the major pathway regulating NAD+ levels in most tissues. The inhibition of this pathway with FK-866 rescues all skin phenotypes observed in Spint1a-deficient larvae as well as in organotypic 3D skin models of psoriasis. Therefore, our results support that the salvage pathway is the one involved in psoriasis and inhibition of this pathway would rescue inflammation. However, we agree that it will be worthy to investigate if other pathways play a role in psoriasis and specifically upon inhibition of the salvage pathway. However, this is out of the scope of this manuscript.
PARG is used in this study, but the protein levels of PARG are not shown, and it is not clear whether the PARG overexpression is sufficient to reduce PAR levels in the models used. AIF pharmacological and genetic manipulation of AIF is used, but it is not shown that AIF translocates to the nucleus in this model.
We agree on these points, so we have analyzed Aifm1 translocation in Spint1a-deficiet larvae and psoriasis patient lesional skin (please, see above our response to reviewer 1) and PARylation upon forced expression of Parga (Fig. 5M).
Does NAMPT inhibition reduce NAPD oxidase activity?
Our results indicate that Nampt inhibition reduce NAPDH oxidase activity, since a drastic reduction of H2O2 production was observed in the skin of Spint1a-deficient larvae treated with FK-866.
PAR plots provided in fig S4 need quantification, and the blots (Fig S4 G&H) should be run on the same gel to make sure the exposure levels are the same. It is not clear which group is represented in lane 4 of Fig S4 G.
We have provided the quantitation. The problem is that we mislabeled the legend of Fig. S4H. The right legend is: 1 +/+, 2 -/- treated with DMSO, 3 -/- treated with FK-866 and 4 -/- treated with olaparib. Therefore, either Nampt or Parp inhibition robustly reduces PARylation of Spint1a-deficient skin to the levels of their wild type counterparts.
Reviewer #3 (Significance (Required)): This study in interesting potentially showing the role of PARP-1 activation and Parthanatos in skin inflammation. It could be very significant if above identified weaknesses are addressed.
We are pleased with this reviewer’s assessment on the significance of our study.
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Referee #3
Evidence, reproducibility and clarity
This study shows NAMPT derived NAD facilitates PARP activation to promote skin inflammation via parthanatos. The authors used the zebrafish model and organoid models of psoriasis and observed that inhibition of NAMPT reduces inflammation in zebrafish and human skin organoid models. They also observed that NADPH oxidase-derived oxidative stress activates PARP, and PARP inhibition or over-expression of PARG or AIF mimics protection mediated by NAMPT inhibition. This is an interesting study, but there are several weaknesses to support the conclusions of this study. While pharmacological inhibition is a powerful tool, complementary methods (knock out of PARP-1) are critical for this paper's conclusions. PARP inhibitor used in this study may not specifically inhibit PARP1 but other PARPs too. Therefore, genetic knockout of PARP will make the make this conclusions/interpretation of this study strong.
Additional comments include:
This study's primary focus is PARP activation and PAR-mediated parthanatos, but it is not shown how different inhibitors used in this study and supplementations of NAD alter PARP activation and PAR formation. NAMPT is not the only NAD biosynthesis pathway; how other NAD pathways respond when NAMPT is inhibited with FK-866 PARG is used in this study, but the protein levels of PARG are not shown, and it is not clear whether the PARG overexpression is sufficient to reduce PAR levels in the models used. AIF pharmacological and genetic manipulation of AIF is used, but it is not shown that AIF translocates to the nucleus in this model. Does NAMPT inhibition reduce NAPD oxidase activity? PAR plots provided in fig S4 need quantification, and the blots (Fig S4 G&H) should be run on the same gel to make sure the exposure levels are the same. It is not clear which group is represented in lane 4 of Fig S4 G.
Significance
This study in interesting potentially showing the role of PARP-1 activation and Parthanatos in skin inflammation. It could be very significant if above identified weaknesses are addressed.
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Referee #2
Evidence, reproducibility and clarity
Summary:
The manuscript entitle "NAMPT-derived NAD+ fuels PARP1 to promote skin inflammation through parthanatos" is well written, divided and organized. This work demonstrated that models of psoriasis are characterized by ROS stress, inflammation and cell death. It was clear that NAMPT, a rate-limiting enzyme of NAD salvage pathway, and PARP1, a Poly-ADP-ribose polymerase, could be targeted to decrease ROS stress and inflammation that are contributing to cell death through parthanatos pathway. However, it was not clear that NAD+ are the responsible for fuel these processes in the psoriasis models analyzed. Nevertheless, the present work demonstrated that the cell death observed in the psoriasis model analyzed was correlated to an unidentified programmed cell death pathway, parthanatos that up to date has not been demonstrated.
Major comments:
Most of the data showed confirmed that inhibition of NAMPT or PARP1 seems to be beneficial for the relief of some characteristics related to oxidative stress and inflammation in the skin. However, the author should show data about NAD+ levels only instead of the ratio NAD+/NADH to state that NAMPT-derived NAD+ is promoting oxidative stress (line 366-368) (fig2K). Some data images are not convincing, or they don't really show an increase or decrease as the author showed in graph data. (Fig1D, 1E - 1F,1G). What is the relevance to analyze muscle and what is the relevance of the results obtained, since the effect of FK-866 in muscle increases the NFKB activity?<br> Figure S4H is not convincing with what the author wrote. The author should make the keratinocyte aggregation experiment with FK-866 treatment to better substantiate what they are proposing.
Minor comments:
Line 281: "NP, a chemical inhibitor of Aifm1 translocation from the nucleus to the mitochondria..." should be the opposite: NP, a chemical inhibitor of Aifm1 translocation from mitochondria to nucleus. Line 299 "figure 6A" should be Figure 6B. How the author explains the relationship between all the results being related to NAMPT and supposedly to NAD+, but an important precursor to make NAD through salvage pathway (NMN) and a well NAD+ booster didn't show any effect? Line 178: should be NAMPT inhibitor stead of FK-866 inhibitor. Line 191-192: I suggest reformulating this sentence since the result showed was only the ratio NAD/NADH.
Significance
The present work greatly demonstrated the relevance of PARP1 and NAMPT in the field of inflammation and ROS in the skin that contribute to diseases like psoriasis. Although it is not a lethal disease, as the author mentioned, it affects the physical and mental health of the individual. Understanding the mechanism that underlie this condition would help to trigger new and more efficient treatments. It was clear that the result showed a promising strategy in targeting NAMPT and PARP1. Furthermore, inhibitor for them is already know and may be useful for future treatment of psoriasis disease.
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Referee #1
Evidence, reproducibility and clarity
Summary:
In this study authors investigated the role of NAMPT, NAD+ and PARP1/parthanatos in skin inflammation using a zebrafish psoriasis model with an hypomorphic mutation of spint1a and human organotypic 3D skin models of psoriasis. Authors showed that genetic deletion and/or pharmacological inhibition of Nampt/PARP1/AIFM1/NADPH oxidases reduced oxidative stress, inflammation, keratinocyte DNA damage, hyperproliferation and cell death in zebrafish models of chronic skin inflammation. Authors also showed the expression of pathology-associated genes in human organotypic 3D skin models of psoriasis with pharmacological inhibition of Nampt/PARP1/AIFM1/NADPH oxidases. The key finding of this study is that PARP1 hyperactivation caused by ROS-induced DNA damage mediates skin inflammation through parthanatos.
Major comments:
This is a very comprehensive study to investigate the role of PARP1 in skin inflammation. The main conclusion was made based on the genetic inhibition and/or pharmacological inhibition of Nampt/PARP1/AIFM1/NADPH oxidases. Although the finding of this study that NAMPT-derived NAD+ fuels PARP1 to promote skin inflammation through parthanatos is interesting and important, there are lots of major concerns and questions, which have to be addressed to better support the main conclusion. In addition, the data and methods were not presented with sufficient detail.
- This study is heavily relied on pharmacology inhibition. However, the specificity and selectivity of many inhibitors were not tested in this study.
- Fig. 1: it is quite confusing how NAD+ increases H2O2 levels? Is NAD+ cell permeable? It is not clear if NAD+ has been really up taken by cells in the larvae. If NAD+ fuels PARP1 to promote skin inflammation, why NAM treatment increased H2O2 levels but NMN precursor failed to increase skin oxidative stress? No reasonable explanation has been provided.
- Fig. 1E and 1G: it is not clear what is the green channel. Similarly, there is no clear description what is red or green in many other figures.
- Fig. 1K and 1L: It is hard to understand why FK-866 reduced H2O2 release, but it increased neutrophils infiltration. How to interpret this conclusion?
- Fig. 2C-D: Why low doses FK-866 reduced neutrophil infiltration whereas high dose FK-866 increased neutrophil infiltration?
- Fig. 2I-J: it is not clear how NF-kB activity was measured. Is that based on green fluorescence shown in Fig. 2J? if so, the representative images were not consistent with the quantification data shown in I. Similarly, many other representative images were also not consistent with their quantification data throughout the manuscript. For example, Fig. 3C/D, 3E/F, 3G/H, 3L/M, Figure S2C/D, S2G/H, Fig. 4C/D, 4J/K.
- Figure S1C, Nampta/Namptb protein expression should be checked and shown after its KO using crispr/cas9 technique.
- Fig. 3I: protein expression of nox1, nox4 and nox 5 should be checked after genetic inhibition using CRISPR/Cas9 technique.
- Fig. 4: If Olaparib treatment increased DNA damage, will it increase PARP1 activation and PAR formation?
- Fig. 4M: it is not clear what staining has been done. No difference was observed among different groups.
- Authors used N-phenylmaleimide (NP) to block AIF nuclear translocation. How does this inhibitor work? what is its actual effect on AIF nuclear translocation? Experiments are required to show this inhibitor actually blocks AIF nuclear translocation.
- Figure S4: it is hard to understand why lane #2 with Olaparib has the highest PAR signal.
- Does spint1a-/- zebrafish show parthanatos cell death? It is not clear how cell death was measured.
- NAD+ levels were regulated by 3 different pathways. Expression of many genes involved in these 3 pathways were altered in psoriasis. However, it is not clear if the other two pathways play a role in PARP1-mediated inflammation.
Minor comments:
- Page 9: To test this hypothesis, we used N-phenylmaleimide (NP), a chemical inhibitor of Aifm1 translocation from the nucleus to the mitochondria (Susin et al., 1996). The statement is not correct.
- Page 12: To the best of our knowledge, this is the first study demonstrating the existence of parthanatos in vivo. This statement is not correct.
- Figure S3 and S6E: they should be presented in an easy understandable way for the general readers.
- Figure legends should be presented in a clearer way.
Significance
Parthanatos is a new type of cell death distinct from apoptosis, necrosis, necroptosis and plays a pivotal role in ischemic stroke and neurodegenerative diseases (Wang Y et a., Science. 2016; Kam TI et al., Science 2018). The current study may provide new evidence of the importance of PARP1 and parthanatos in skin inflammation and potential targets for the treatment of skin inflammation.
The reviewer has the expertise in oxidative stress, PARP1 and parthanatos research.
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Reply to the reviewers
We thank the reviewers for the positive assessment of our work and for the constructive comments that helped us to improve the quality of our manuscript. We have carefully considered each point and have addressed most by modifying the manuscript text to increase clarity of our work. Based on a suggestion by Reviewer 2 we have also included the results of a new experiment.
In addition to addressing all comments of the reviewers, we have expanded the part of the study analysing the functionality of Caulobacter’s DnaA Nt in the heterologous host E. coli. Furthermore, we have replaced our original set of fluorescence data by a new data set that has been acquired using optimized measurement parameters (bottom read and 100 for the detector gain - see Material and Methods for details), which have improved the signal-to-noise ratio and the overall quality of the fluorescence profiles. Importantly, these new data do not change, but rather strengthen, our conclusions.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
Felletti et al provide compelling new evidence that a CDS element in the dnaA mRNA is required for nutrient dependent translationol control. This provides a mechanisms by which dnaA translation is shut off during carbon starvation, and is supported by a rather rigorous analysis of the mRNA performed both in vitro and in vivo. Overall it was a pleasure to read and the data are generally very compelling. My specific comments are below:
**Major Comments:**
While the authors rule out differences in charging of different ala-tRNAs as controlling the nutrient dependent repression in translation, the authors assume that this must be due to the nascent sequence. However, could it also be possible that all ala-tRNA isoacceptors have lower charging after C-starvation?
We thank the reviewer for raising this important point. As Reviewer 1 pointed out, we cannot conclusively exclude that carbon starvation could lead to reduced charging levels of all isoacceptor Ala-tRNAs. However, based on the available literature, we consider it unlikely. In a first work by Elf et al 2003 (confirmed later by Dittmar et al 2005 and Subramaniam et al 2014) the authors argued that under amino acid-limiting conditions the charging levels of the different isoacceptor tRNAs depend directly on their codon usage during translation. Importantly, in our work we could show that Nt mediates the inhibition of translation independent of the synonymous codon choice, suggesting that aa-tRNA levels are not limiting in our experimental conditions. To address this comment of Reviewer 1, we discussed this matter in a greater detail in the revised version of the manuscript (line 374-379).
**Minor comments:**
It was observed many years ago that tmRNA is required for the proper timing of DNA replication initiation in Caulobacter (Cheng and Keiler J Bact 2009). Since the AAI motif is appearing to alter translation elongation, it might be interesting to discuss the AAI motif may be linked to ribosome arrest and rescue.
We appreciate this suggestion. Cheng and Keiler 2009 proposed an indirect involvement of the tmRNA in the transcriptional regulation of DnaA over Caulobacter’s cell cycle. In the revised version of the manuscript, we mention the tmRNA and ArfB protein as possible factors involved in ribosome rescue following Nt-induced ribosome stalling and we refer to Keiler et al 2000 and Feaga et al 2014.
Line 49 - add "initiation"
The word “initiation” was added to the text.
Line 61 - is "cleared" meant to be proteolyzed or simply meaning to have a lower protein level?
We apologize if we were not clear. We rephrased the text as follows: “[…] DnaA levels decrease at the onset of carbon starvation […]”.
Line 92-93 - is this 5' UTR based on a previously defined TSS determined in their previous study?
dnaA TSS has been first determined by primer extension (Zweiger and Shapiro 1994) and later by global 5’RACE (Schrader et al 2014 and Zhou et al 2015). In the new version of the manuscript, we include references to these previous studies (line 94).
Line 115-118 - this is interesting, might this conserved 5' UTR be added to rfam?
We thank the reviewer for this suggestion. We will submit our alignment to rfam after publication of the manuscript in a journal.
Line 126-127, 131,189 - Is the 3nt sequence the authors found here considered a Shine-Dalgarno site? I would imagine that this would be too small to consider this. Perhaps calling it SD-like sequence might be more appropriate.
We agree with this comment. In the new version of the manuscript, we refer to the identified 3-nucleotide sequence as a “SD-like sequence”.
Lines 136-140, 208-210 - Would the authors consider this upstream site with a potential CUG start codon a standby site? It appears to fit many of the criteria which could be used to define one.
According to our probing data, the mRNA region in proximity of the CUG start codon forms a very stable stem-loop structure. Based on our previous experience (especially the extensive work by the Wagner lab), typical ribosome standby sites only occur in largely unstructured regions. Furthermore, in Supplementary Fig. 4 we show that the deletion of stem P4 does not affect eGFP expression levels. For these reasons, we consider it unlikely that the putative CUG start codon is part of a ribosome standby site.
Lines 253-255 - this is a beautiful experiment, but very hard to understand from the text. Perhaps add a sentence or two to explain it in more detail.
We thank the reviewer for this comment. In the revised version of the manuscript, we provide a more detailed description of the dfsNt reporter mutant. We hope this will address the reviewer’s concerns.
Line 307 - add "synonomous"
The word “synonymous” was added in the revised version of the manuscript
When dnaA is depleted, it was observed that the chromsome can be erroneously segregated by the ParA/B/S system (mera et al PNAS). Does this occur in C-starvation when DnaA levels drop?
In a separate study we have also observed that in a fraction of DnaA depleted cells the origin of replication is erroneously translocated from the stalked to the swarmer cell pole. We have not studied this phenomenon under carbon starvation, as it lies outside the scope of this paper. However, if the ParA/B/S remains functional under carbon starvation, this might also happen in G1-arrested starved cells.
Reviewer #1 (Significance (Required)):
Appears to be quite significant to researchers studying regulation of bacterial cell cycle and translation. Since DnaA is conserved across bacteria, and this mechanism works in E. coli, it appears that the findings will likely be important in many bacterial systems.
Referee Cross-commenting
All the reviewer comments I read seem reasonable. Specifically, I found the point about E. coli 30S ribosomes is very important that the authors address. This could be done in writing, but should be better listed as a caveat to those experiments.
As suggested by the reviewers, we have partially rephrased some parts of the text describing the toeprint results. Moreover, we have inserted in the main text and in Fig. 1 legend explicit references to the use of purified E. coli 30S subunits and tRNA-fMet. We believe these changes will address the reviewers’ concerns.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
**Summary:** The Jonas lab provide good evidence that they have found a new mechanism to regulate the amount of the DnaA protein by a starvation signal. The DnaA protein is the key chromosome replication initiator probably for most bacteria and as such DnaA is the target of many regulatory inputs. The authors created an accurate reporter system that allows them to dissect the 5' mRNA translated and untranslated sequences of dnaA and they have convincingly demonstrated that the N-terminal DnaA peptide sequence and not the RNA mediate the response to starvation by glucose exhaustion. This is potentially a model example for global translational responses in bacteria.
**Major comments:**
The main conclusion, i.e. that the DnaA leader peptide "Nt" mediates this response is convincing. However, there were 2 major problems that should be easily addressed. These do not subtract from the main conclusion.
Problem 1
E. coli 30S subunits were used in the "Toeprint" assay of Fig. 1. Obviously Caulobacter 30S Ribosome subunits should have been used, or a justification should be given. One remedy would be to make this supplementary information.
We thank Reviewer 2 for this comment. We agree that it would be better to use Caulobacter 30S ribosome subunits in our toeprint experiments. However, because toeprint assays with E. coli 30S ribosome were already established in our lab (i.e. the Wagner lab, where the assays were performed) and because works by other groups have shown that E. coli 30S subunits can be used to study the translation of mRNAs from other bacteria, we decided to use this experimental set up. Based on our results, we also had no reason to doubt the suitability of the E. coli 30S subunits. The toeprint showed that translation starts at the in silico predicted translation start site, which was further confirmed by our in vivo mutagenesis experiments. For these reasons, we are confident that the toeprint assays indicate the true translational start site. However, we acknowledge that we could have been more explicit about the use of the purified E. coli 30S subunits and tRNA-fMet in toeprinting assay. To increase clarity and transparency, in this revised version of the manuscript, some parts of the main text were rephrased and references to the use of E. coli 30S and tRNA-fMet were introduced (including Fig. 1 legend). We hope that these changes will address the reviewer’s concerns.
Problem 2
The results in Fig. 6B could be due to the Nt simply making the hybrid protein more unstable in E. coli. This is the main impression given by the drop in signal. In this case, the conclusion would be wrong, and Nt is not transferring a starvation translation block from C. crescentus to E. coli. Nt is just making the protein unstable. These results should be treated as preliminary pending protein stability measurements. However, this defect does not subtract from the other main points and without the Fig. 6 E. coli experiments they still make a complete and interesting story. One remedy would be to make this also supplementary information.
It is indeed striking that a drop of normalised fluorescence is observed for the 5’UTRdnaA-Nt construct in E. coli but not in Caulobacter. In order to address if this behavior can be explained by reduced protein stability, we have performed a translation shut-off assay using the 5’UTRdnaA-Nt E. coli reporter construct. The results of this experiment (shown in Supplementary Fig. 9A and described in line 327-329) show that the normalised fluorescence remains stable over 10 hours after chloramphenicol addition to the culture, ruling out that the presence of Nt significantly affects eGFP protein stability in E. coli. Importantly, this experiment also showed that in contrast to the chloramphenicol treated culture, in which the OD600 decreased after reaching stationary phase, the OD600 of the non-treated cultures slightly increased between 2 and 10 hours (Supplementary Fig. 9A). Because this increase was not observed in carbon starved Caulobacter cultures, we consider the different growth dynamics between E. coli and Caulobacter to be the most likely explanation for differences in eGFP accumulation at later time points during the experiment.
To further strengthen our E. coli data, we have analysed additional relevant Nt mutants that we identified as most critical mutants in our Caulobacter experiments presented in Fig. 5, namely dfsNt, mutD1, mutD2, ΔAAI and AAI>DDK. Determination of Δt and Δf values for the E. coli strains carrying these different Nt constructs showed similar results as for the corresponding constructs in Caulobacter. Collectively, these new data further support the notion that Nt operates in E. coli through a conserved inhibitory mechanism of translation. These data are now included in a reorganized new version of Fig. 6 (panels A, B) as well as in Supplementary Fig. 9.
**Minor comments:**
There are also 6 minor issues that are easily addressed, most by small changes to the text, and these should improve this otherwise fine manuscript.
Issue 1
Line 88 Fig. 1A shows DnaA degradation upon entering stationary phase from a low glucose media and not a simple starvation response to one component like glucose. Did the authors consider trying simple washout experiments, i.e. resuspend the cells in glucose-free media? This would have the advantage of suddenly exposing the cells to starvation and thereby studying the sudden response rather than the slower lingering response which would be due to many factors and not just glucose removal.
In a previous work from our lab (Leslie et al 2015), we have conclusively shown that the downregulation of DnaA synthesis depends primarily on the nutrient content of the growth medium.
Besides being in continuity with our previous work, we think that the starvation protocol that we used in the present study, and that was also used by the Sean Crosson lab (Boutte et al. 2012), might better reproduce what happens in the natural environment when nutrient levels gradually decrease until becoming limiting for bacterial growth.
Issue 2
Reference 16 should be cited are the first publication to show that glucose and other starvations induce DnaA degradation in Caulobacter.
We have added Reference 16 to the first sentence of the results section, in which we state that DnaA levels decrease when cells are shifted from a glucose-supplemented minimal medium to a glucose-limiting medium.
Issue 3
Fig. 1D shows that the TOEprint is not changed by adding the ribosome, very surprising considering its size and SD docking & alignment. 2 Minor bands then appear when the tRNA-Met is further added. These are presumably the "toeprints". A control with just the added tRNA-Met would make this result much more significant.
In the existing literature, there is a common consensus to consider real toeprints (i.e., indicative of the presence of an assembled translation pre-initiation complex) as only those bands that appear faintly in the presence of the 30S ribosome subunit but that become clearly enhanced upon addition of the initiator tRNA-fMet. Some examples can be found in Hoekzema et al 2019, Romilly 2014, Romilly 2020. In cases when the translation start site is buried in a structural element, the intensity of the toeprint signal is further increased when the mRNA is rendered unfolded, as seen in our data.
tRNA-30S-independent bands always show up in toeprint experiments, but their intensities differ with the sequence of the mRNA and sometimes the choice of RT used for primer extension. Addition of initiator tRNA-fMet alone is commonly not done in toeprint experiments (see references mentioned above). Finally, we want to point out again (see also our answer on “Problem 1”) that the toeprint data are very much consistent with our in silico predictions and our in vivo mutagenesis data. Therefore, we are confident that the observed toeprint upstream of the AUG corresponds to the true ribosome binding site.
Issue 4
Why does the cell OD drop, e.g. in Fig. 2, is it cell death from starvation?
We don’t think that the slight reduction of OD600 observed in our experiments is due to cell death. Based on our knowledge, carbon starved cells remain viable up to 24 hours after the starvation onset. Instead, we have observed a cell volume reduction, which may at least partially explain the observed OD600 decrease.
Issue 5
Line 327 Discussion "This study reveals a new mechanism, by which some bacteria can regulate the synthesis of the replication initiator DnaA in response to nutrient availability by modulating the rate of translation." Rate of translation or rate of translation abortions (as implied in Fig. 6)?
The rate of translation is the result of multiple contributions such as initiation, elongation, abortion and termination. Our data indicate that Nt is a regulator of DnaA translation elongation responding specifically to the nutritional state of the cell. Translation abortion could be one of the possible outcomes (but not the only one) of ribosome stalling. For these reasons, in the new version of the manuscript, we added the word “elongation” at the end of the sentence mentioned by Reviewer 2 (line 354).
Issue 6
It seems that that for most experiments with the eGFP the translation and protein decay components of the signal could have been easily uncoupled by running a parallel +chloramphenicol control. For example, this would simplify the interpretation of Fig. 6 where Nt eGFP stabilities are an issue and it is important to establish that comparable protein stability with and without the Nt peptide.
To address the reviewer’s comment, we have now included a chloramphenicol control experiment (stability assay) performed with E. coli carrying the 5’UTRdnaA-Nt reporter construct (Supplementary Fig. 9A). Please, see the response above for more details. For the experiments with the Caulobacter 5’UTRdnaA-Nt reporter we show in Supplementary Fig. 7 that the Nt peptide has no destabilising effect on eGFP.
Reviewer #2 (Significance (Required)):
Caulobacter crescentus is a model bacterium that has provided many insights into bacterial physiology that are now exploited to understand many organisms. These present results may provide one such example. It is known that the first amino acids of translated peptides can influence increase or impede exit from the ribosome, so this is a potential translation-level regulatory point that might be used by many organisms. This manuscript gives a concrete and important example of such usage suggesting that it many be widespread. Therefore, this work should find a wide audience and it should stimulate research in many other systems.
My lab also studies Caulobacter crescentus and we studied the same dnaA gene and protein including starvation responses. We at present do not have projects on dnaA but we do study other regulators and regulatory mechanisms of chromosome replication in Caulobacter crescentus.
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Referee #2
Evidence, reproducibility and clarity
Summary:
The Jonas lab provide good evidence that they have found a new mechanism to regulate the amount of the DnaA protein by a starvation signal. The DnaA protein is the key chromosome replication initiator probably for most bacteria and as such DnaA is the target of many regulatory inputs. The authors created an accurate reporter system that allows them to dissect the 5' mRNA translated and untranslated sequences of dnaA and they have convincingly demonstrated that the N-terminal DnaA peptide sequence and not the RNA mediate the response to starvation by glucose exhaustion. This is potentially a model example for global translational responses in bacteria.
Major comments:
The main conclusion, i.e. that the DnaA leader peptide "Nt" mediates this response is convincing. However, there were 2 major problems that should be easily addressed. These do not subtract from the main conclusion.
Problem 1
E. coli 30S subunits were used in the "Toeprint" assay of Fig. 1. Obviously Caulobacter 30S Ribosome subunits should have been used, or a justification should be given. One remedy would be to make this supplementary information.
Problem 2
The results in Fig. 6B could be due to the Nt simply making the hybrid protein more unstable in E. coli. This is the main impression given by the drop in signal. In this case, the conclusion would be wrong, and Nt is not transferring a starvation translation block from C. crescentus to E. coli. Nt is just making the protein unstable. These results should be treated as preliminary pending protein stability measurements. However, this defect does not subtract from the other main points and without the Fig. 6 E. coli experiments they still make a complete and interesting story. One remedy would be to make this also supplementary information.
Minor comments:
There are also 6 minor issues that are easily addressed, most by small changes to the text, and these should improve this otherwise fine manuscript.
Issue 1
Line 88 Fig. 1A shows DnaA degradation upon entering stationary phase from a low glucose media and not a simple starvation response to one component like glucose. Did the authors consider trying simple washout experiments, i.e. resuspend the cells in glucose-free media? This would have the advantage of suddenly exposing the cells to starvation and thereby studying the sudden response rather than the slower lingering response which would be due to many factors and not just glucose removal.
Issue 2
Reference 16 should be cited are the first publication to show that glucose and other starvations induce DnaA degradation in Caulobacter.
Issue 3
Fig. 1D shows that the TOEprint is not changed by adding the ribosome, very surprising considering its size and SD docking & alignment. 2 Minor bands then appear when the tRNA-Met is further added. These are presumably the "toeprints". A control with just the added tRNA-Met would make this result much more significant.
Issue 4
Why does the cell OD drop, e.g. in Fig. 2, is it cell death from starvation?
Issue 5
Line 327 Discussion "This study reveals a new mechanism, by which some bacteria can regulate the synthesis of the replication initiator DnaA in response to nutrient availability by modulating the rate of translation." Rate of translation or rate of translation abortions (as implied in Fig. 6)?
Issue 6
It seems that that for most experiments with the eGFP the translation and protein decay components of the signal could have been easily uncoupled by running a parallel +chloramphenicol control. For example, this would simplify the interpretation of Fig. 6 where Nt eGFP stabilities are an issue and it is important to establish that comparable protein stability with and without the Nt peptide.
Significance
Caulobacter crescentus is a model bacterium that has provided many insights into bacterial physiology that are now exploited to understand many organisms. These present results may provide one such example. It is known that the first amino acids of translated peptides can influence increase or impede exit from the ribosome, so this is a potential translation-level regulatory point that might be used by many organisms. This manuscript gives a concrete and important example of such usage suggesting that it many be widespread. Therefore, this work should find a wide audience and it should stimulate research in many other systems.
My lab also studies Caulobacter crescentus and we studied the same dnaA gene and protein including starvation responses. We at present do not have projects on dnaA but we do study other regulators and regulatory mechanisms of chromosome replication in Caulobacter crescentus.
-
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Referee #1
Evidence, reproducibility and clarity
Felletti et al provide compelling new evidence that a CDS element in the dnaA mRNA is required for nutrient dependent translationol control. This provides a mechanisms by which dnaA translation is shut off during carbon starvation, and is supported by a rather rigorous analysis of the mRNA performed both in vitro and in vivo. Overall it was a pleasure to read and the data are generally very compelling. My specific comments are below:
Major Comments:
While the authors rule out differences in charging of different ala-tRNAs as controlling the nutrient dependent repression in translation, the authors assume that this must be due to the nascent sequence. However, could it also be possible that all ala-tRNA isoacceptors have lower charging after C-starvation?
Minor comments:
It was observed many years ago that tmRNA is required for the proper timing of DNA replication initiation in Caulobacter (Cheng and Keiler J Bact 2009). Since the AAI motif is appearing to alter translation elongation, it might be interesting to discuss the AAI motif may be linked to ribosome arrest and rescue.
Line 49 - add "initiation"
Line 61 - is "cleared" meant to be proteolyzed or simply meaning to have a lower protein level?
Line 92-93 - is this 5' UTR based on a previously defined TSS determined in their previous study?
Line 115-118 - this is interesting, might this conserved 5' UTR be added to rfam?
Line 126-127, 131,189 - Is the 3nt sequence the authors found here considered a Shine-Dalgarno site? I would imagine that this would be too small to consider this. Perhaps calling it SD-like sequence might be more appropriate.
Lines 136-140, 208-210 - Would the authors consider this upstream site with a potential CUG start codon a standby site? It appears to fit many of the criteria which could be used to define one.
Lines 253-255 - this is a beautiful experiment, but very hard to understand from the text. Perhaps add a sentence or two to explain it in more detail.
Line 307 - add "synonomous"
When dnaA is depleted, it was observed that the chromsome can be erroneously segregated by the ParA/B/S system (mera et al PNAS). Does this occur in C-starvation when DnaA levels drop?
Significance
Appears to be quite significant to researchers studying regulation of bacterial cell cycle and translation. Since DnaA is conserved across bacteria, and this mechanism works in E. coli, it appears that the findings will likely be important in many bacterial systems.
Referee Cross-commenting
All the reviewer comments I read seem reasonable. Specifically, I found the point about E. coli 30S ribosomes is very important that the authors address. This could be done in writing, but should be better listed as a caveat to those experiments.
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Reply to the reviewers
The authors wish to thank all three Reviewers for their appreciative comments regarding our ECPT and for very useful suggestions. Response to all points raised are presented below, we hope that the responses and new experiments proposed in the following pages will fully address remaining concerns.
Reviewer’s comments to the BiorXiv paper by Chesnais et al, 2021
“High content Image Analysis to study phenotypic heterogeneity in endothelial cell monolayers”
https://www.biorxiv.org/content/10.1101/2020.11.17.362277v3
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
The authors highlight the importance of endothelial heterogeneity using endothelial cells from different tissues. They examined aortic and pulmonary endothelium as well as HUVECs. They cultured the cells in identical conditions and also stimulated them with a physiological concentration of vascular endothelial growth factor as well high concentrations as would be found in cancers. They developed a profiling tool that allowed analysis of individual endothelial cells within a monolayer and quantification of inter-endothelial junctions, Notch activation, proliferation and other features.
**Major comments**
1. It would be useful to apply this technology one step beyond two-dimensional culture, to use vessels opened up longitudinally so that one can see the monolayer of endothelial cells and assess whether it is relevant in primary material in situ. I think this would be a major utility of the whole approach.
R: We thank this reviewer for the suggestion. In vivo analysis is not in the objectives of the paper. However, we propose to perform “En face” staining of murine blood vessels following the protocol in the reference below. We will perform stainings for murine CDH5 (VE-Cadherin), NOTCH1 intracellular domain, HES1 and DNA which parallel that used in vitro on human EC. We will then apply our revised ECPT workflow and present data in a new Figure.
En Face Preparation of Mouse Blood Vessels. Ko KA, Fujiwara K, Krishnan S, Abe JI. J Vis Exp. 2017 May 19;(123):55460. doi: 10.3791/55460. PMID: 28570508
2. There are some very nice images here but disappointed not see a field that could show staining and markers for several of the target proteins and thus show the heterogeneity and randomness or organisation of the endothelial cells.
R: We thank the reviewer for the appreciative comment. We propose to include representative microphotographs to illustrate the heterogeneity of different EC monolayers in the revised version of the manuscript. Furthermore, to further illustrate these aspects we will also include spatial correlation maps of cells and features measured with ECPT as explained below.
3.
- The Notch signalling is an important aspect of this work, particularly evidence of lateral inhibition would have been of value. For example, one might expect cells adjacent to each other to have alternating high and low NICD. R: We thank the reviewers for the suggestion. To address this, we are currently developing a new module to perform spatial autocorrelation analysis based on cell maps built using ECPT. In particular we have developed a new module to export cell maps as spatial objects in R which can be then analysed using the adespatial R package and provide correlation metrics such as the Moran’s autocorrelation index (see reference below). The index works with continuous data, removing the need to establish arbitrary thresholds and thus provides formal metrics to demonstrate heterogeneity in EC monolayers. We have derived this index as an example of such analysis for synthetic data and for one ECPT cell map as shown below.
Figure 1: Moran’s spatial autocorrelation analysis using R and adespatial package. Moran’s index has values between –1 and 1. If adjacent cells had a consistent tendency to acquire alternate high and low NICD values, the corresponding bivariate Moran’s index would have an I+ value ~ 0 and an I- value approaching -1. In the example cell map both I+ and I- have relatively small absolute values and large p values which suggest a random cell distribution. The analysis was performed on synthetic data and ECPT derived data (HUVEC at baseline).
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Community ecology in the age of multivariate multiscale spatial analysis
S Dray et al, Ecological Monographs, 2012. doi:10.1890/11-1183.1
- NICD staining alone does score the extent of the signalling because of many factors that can influence the transport of the cleaved NICD. Really a marker of Notch signalling downstream e.g. HES or HEY family, DLL4 fis needed to give more information about this critical aspect. R): We thank the reviewer for the suggestion. We are currently performing HES1 staining (with no Pha staining) along with a new NICD mAb (see below). Preliminary qualitative data (Fig 2) show that HES1 staining also reveals single cell heterogeneity of NOTCH activation in the same monolayer. We will include ECPT analysis of HES1 and correlation with NICD and other features as suggested. We will reformat the current Fig 5 to include HES1 analysis and improved metrics of NOTCH pathway activation including spatial analysis (point 3 above).
Figure 2: HES1 immunostaining on HUVEC (Image enhanced for visualisations). Cell nuclei labelled as 1, 2 and 3 have raw mean grey values of HES1 signal equal to 2271, 11210 and 48261 (C2/C1 and C3/C2 >4 folds).
I really do not think that in Figure 5 it is justified to have a red line drawn through the cloud of points. The correlation coefficient is so low that this is meaningless. The failure to distinguish a P value from biological relevant is worrying. Much better comparison would have been between NICD staining and a downstream gene regulated by notch.
R: We appreciate the reviewer’s concerns and are presenting our analyses of NOTCH activation using new immunostainings (HES1) and robust metrics for NOTCH activation as discussed above. We will therefore remove the mentioned corelation plots from the reviewed version of the manuscript.
It is important to know that the antibodies used for staining have be validated by the investigators. They would need to show a single band on Western blots or be able to block staining on immunohistochemistry. We all know the manufacturers can be unreliable and use high concentrations of proteins for Western blots. These should be added as a supplementary figure.
R: While the paper was under revision the AB8925 (NICD, Abcam) has been retracted from the market. To address this major concern, we have decided to acquire a different antibody targeting the intracellular portion of NOTCH receptor and validated its specificity by western blot. Fig 3 below, show western blots demonstrating a clean band at ~98 Kd as expected for cleaved NOTCH1 intracellular domain (NICD).
We are currently repeating the whole experiment presented in the current version of the manuscript and the ECPT analysis using the new antibody and including HES1 one of the canonical NOTCH target genes as also suggested by this and other Reviewers. We will provide WB analysis of all antibodies used in the paper in a supplementary figure in the revised manuscript.
Figure 1, WB analysis (NOTCH1 intracellular domain, AB52627, Abcam). of HUVEC (lanes 2,3), HAoEC (lanes 4,5) and HPMEC (lanes 6,7)
Reviewer #1 (Significance (Required)):
This represents a valuable and thorough methodology likely to be highly useful to many groups and show new insights into endothelial biology.
Wide audience, cancer, cardiology, vascular disease-covid.
My expertise >100 papers on angiogenis in cancer, basic mechanism, therapy models, bioinformatics IHC, patients, clinical trial. H score 190 Google Scholar
R: We thank Reviewer One for their very appreciative comments and we hope that the proposed revisions will fully address remaining concerns.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
The manuscript by Chesnais et al reports development of workflow for analysis of cultured endothelial cells , which they call Endothelial Cell Profiling tool (ECPT). Using ECPT they analyse several parameters in three different endothelial cell types (HuAEC, HUVEC and HPMEC), such as cell morphology, activation of cytoskeleton, VE-cadherin junctions, cell proliferation and Notch activation, under steady conditions and upon treatment with VEGF. The analysis allows to observe some predicted changes, such as increase in cell cycle and junctional activation in cells treated with VEGF-A, and such changes are highly heterogeneous. Overall, this is a potentially useful albeit not revolutionary tool for batch analysis of cultured endothelial cell phenotypes.
I have the following comments:
- To make their case the authors should provide a comparison with other currently used approaches for EC phenotypic analysis in vitro - what is the advantage of using ECPT? The authors repeatedly use the term "single-cell level of analysis ", but this is in fact the case of any IF based analysis of cultured cells.
R: We thank the reviewer for the suggestions. Indeed, several tools for imaging based single cell phenotyping are available. However, ECPT represents an improvement under several aspects. First, it allows improved segmentation of difficult-to-segment and heterogeneous cells; second, ECPT allows multi-parametric analysis on large image datasets in a semi-automated and structured way facilitating downstream data analysis; third, ECPT is open source.
Furthermore, ECPT is a very flexible workflow including tools which facilitate and automate several tasks such as systematic images re-labelling and grouping. We will now draft a table including a complete list of features and improvements in comparison to other available tools and include it in revised manuscript in appendix1 and include analyses which are not implemented in any currently available software such as spatial autocorrelation.
I strongly recommend to stain HPMECs for PROX1, these cells are frequently 100% lymphatic endothelial cells. In this case the authors compare different lineages and not blood endothelial cells from different locations.
R: We thank the reviewer for the suggestion. We will address this with a new characterisation as supplementary figure in the revised manuscript. We are currently performing a qRT-PCR screening of several EC marker including arterious, venous and lymphatic markers (e.g., CXCR4, Tie2, CDH5, PROX1, LYVE1 as well as baseline NOTCH1 and Dll4 and downstream genes such as HES1 and HEY2.
Please provide evidence for specificity of NICD antibody.
R: We thank this reviewer for the suggestion. Please see response to Reviewer one point 5.
Figure 1: HPMEC picture appears out of focus
R: We thank this reviewer for noticing, we will now include a clearer picture in revised version of the manuscript.
Figure 3 A - it is not entirely clear what is the difference between activated and stressed phenotype, they look quite similar.
R: We will clarify the definitions of cell activation in revised version of the manuscript and present this analysis as supplementary material to demonstrate the flexibility of our ECPT rather than in main figures. We have removed Pha staining from the new experiments we are performing to allow HES1 staining and address NOTCH signalling in more details. The assessment of Pha and stress fibres in previous experiments will be moved to supplementary material. The classification is based on PhA staining using CPA classifier which was trained to distinguish among the two by the presence of stress fibres. The general rule to place cells in the stressed category during training of the CPA model was the observation of stress fibres crossing the nucleus while cells with peripheral bundles of actin were placed in the activated category.
Figure 5 - what is the difference in NICD localization between "high" and "On" conditions?
R:
Since it has been noted by this and other reviewers that this classification might be difficult to interpret and in fact, the established thresholds are somehow arbitrary, we will completely revise the way we present analysis of NOTCH activation data including downstream analysis and more formal metrics of spatial correlation and extent of activation eliminating the need to impose thresholds (also see response to Reviewer one point 3).
Since the authors make a correlation between Notch activity and junctional stabilization, it would be important to confirm this by other means, such as analysis of Notch target genes.
R: We thank this reviewer for the comment which resonate with this and other Reviewers’ comments. We will include HES1 analysis in the revised manuscript, please see Response to point 6 and reviewer’s one point 3 above.
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**Technical and minor**
1. Methods mentions HDMECs (human dermal microvascular endothelial cells) but the authors discuss HPMEC throughout the text 2. Please add scale bars on all microscopy pictures. 3. Please provide the information on what isoform of VEGF-A was used for stimulation and the rationale for selecting the concentration.
R: We thank this reviewer for flagging these imprecisions and we will fix them in revised version of the manuscript.
Reviewer #2 (Significance (Required)):
The authors provide a workflow for the phenotypic analysis of cultured cells. Such tool is potentially useful, although the examples the authors show do not reveal striking examples of why such analysis is better in comparison to existing approaches. My guess is that the analysis may be faster and less tedious, once the training sets are generated, but this is not specified. My speciality is endothelial cells biology.
R: We thank this reviewer for their very useful and appreciative comments. As mentioned above we will expand appendix 1 to fully explain potential and utility of our ECPT and review the main text to clearly highlight main advantages.** We hope that our plan for revision will fully address remaining concerns.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
**SUMMARY:**
The manuscript by Chesnais et al. presents a novel endothelial cell (EC) profiling tool (ECPT) which provides spatial and phenotypic information from individual ECs, and was tested with a variety of specialized EC subtypes (arterial, venous, microvascular). They present a high throughput immunostaining and imaging-based platform using culture of human ECs on 96-well plates and capture of fixed, stained samples on a Perkin Elmer Operetta CLS system. The authors report the use of this ECPT tool to investigate EC phenotypes from human umbilical vein ECs (HUVEC), human aortic ECs (HAoEC) and human pulmonary microvascular (HPMEC) in relation to 50 ng/mL VEGF stimulation for 48 hours, and the general parameters of proliferation, Notch activation and stress fiber rearrangement (F-actin), and present this as a prospective platform to examine differences in EC phenotypes and responses at a more individualized level.
**MAJOR COMMENTS:**
1. Fundamentally, the advantage of single cell technologies is the ability to segregate populations to make novel observations. One area that would be of interest to explore in this manuscript using this ECPT platform would be reporting the results from single cell analysis that is then subsequently pooled within a sub-population, rather than sub-stratifying populations to reflect the multiple phenotypes that may be present within a single "confluent" well. With analysis of EC heterogeneity, it would be of interest to differentiate heterogeneity within EC subtypes at the culture/treatment conditions presented, and heterogeneity between EC subtypes.
R: We thank this reviewer for the suggestions, we believe that the new approach to evaluate heterogeneity through spatial autocorrelation can provide a much better and clearer picture of this aspect (see responses to Reviewers One point 3 and Two points 6 and 7. Furthermore, we are currently restructuring the ECPT data structure to a more intuitive layout (list of lists rather than a single huge data frame) without affecting downstream data presentation. We will also update our Shiny App to enable the user to perform analyses on data subsets of interest without any R coding, we will present examples and walkthrough of this approach in appendix.
2.
The term "stable IEJ" is used and refers to 48h after seeding 40,000 cells on a 96-well plate, but it is unclear how the authors defined or demonstrated a "stable" junction. In previous reports, longer-term culturing of EC monolayers well beyond the point of confluence has been shown to result in junctional complex rearrangement (Andriopoulou P et al. Arterioscler Thromb Vasc Biol. 1999; reviewed in Bazzoni G & Dejana E. Physiol Rev. 2004). To this point, the fact that the different EC subtypes investigated had different percentages of "quiescent cells" suggests that the monolayers were not completely quiescent. The statement that the IEJ classification is "an immediate index of EC activation in contrast to quiescence" should be further supported by references or data. The definition of quiescent EC as simply non-proliferating, non-migrating is somewhat reductionist, and oversimplifies EC states. The authors state that HAoEC and HUVEC "...appeared more active...", but it is unclear what "active" means, and whether this may simply reflect that these cells had not yet reached confluence or quiescence in the 48h total culture time. As well, it is unclear how "migratory phenotypes" could occur in confluent monolayers. It would be helpful to see the data for these observations. If leaving ECs longer in culture, are the authors able to achieve a higher percentage of quiescent cells?
R: We thank this reviewer for the very insightful comments and for suggesting the references. Indeed, we considered these aspects carefully. Regarding cell culture density and confluency, we previously tested seeding densities of 30000-60000 cell/well of 96 well plates (0.32 cm2, ~95000-190000cells/cm2) and we selected 40000 as the maximum seeding density allowing adhesion of >99% of cells. For HUVEC, a seeding density of 40000 cells/well (125000 cells/cm2) produced a high-density culture immediately after seeding (close to what reported for long-confluent cultures in Andriopoulou P et al, ATVB 1999, 140000 cells/cm2). We allowed further 48h culture aiming to achieve junctional “stabilisation” and “maximal” cell density. For consistency, we also seeded 40000 HAoEC and HPMEC per well in all our experiments, however both cell types are significantly larger than HUVEC (Fig 4). For all cells cultures we used EGM2 medium which has few differences with that reported in Andriopoulou P et al, namely, absence of antibiotics and antimycotics and use of defined cocktail of recombinant growth factors instead of Endothelial Cells Growth Supplement. In the past we compared HUVEC cultured in EGM2 and supplemented M199 medium and in our experience EGM2 promotes higher proliferation rates in sub-confluent cultures but similar morphology upon confluency. Is notable that several other factors (including flow, matrix, perivascular cells) are absent in our culture conditions and therefore the homeostatic balance found in vivo might not be fully achievable under our experimental conditions. However, we argue that the described culture conditions should be sufficient to reach a bona fide relatively quiescent EC phenotype in culture.
Save these considerations, we agree with this reviewer that providing examples of longer-term cultures would help substantiating our findings and further validate the ECPT approach. We will perform a supplementary experiment to evaluate this aspect by comparing 48h cultures with longer culture times (72h and 96h). Furthermore, we will expand the methods section with the details discussed above and in relation to the suggested references.
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Regarding the definition of “stable IEJ” and “active EC”, we used this terminology referring exclusively to our measures of IEJ stability (STB index) and Pha based cell classification where we used the terms of “quiescent”, “active” or “stressed”. Therefore, all statements mentioning more or less “stable IEJ” or “active” EC are relative to the specific context of our experiment (not in absolute terms).
Overall, we appreciate that the terminology we employed is a source confusion and might suggest inappropriate over-interpretation of our results. We will correct the text in the manuscript to avoid this confusion and to clarify that our observations are valid within the context of our in vitro conditions. In particular, we will present the data regarding junctions as proportions of different junction per cell, and we will rename cell “activation” categories based on PhA immunostaining using more neutral terms (e.g., No Fibres, Peripheral Bundles, Stress fibres). Finally, we will also attempt to generalise our observations to more physiologic context by performing immunostaining on “en face” preparation of murine blood vessels (cfr response to R1 point 1).
Fig 4: Cell area density distribution for HUVEC, HAoEC and HPMEC in baseline conditions.
Could the authors comment on the baseline NICD immunoreactivity in the nuclei in HAoEC and HPMEC compared to HUVEC? Is this a reflection of active NOTCH signaling? Or rather, is it possible contact-inhibition (and downregulation of NOTCH) may not have occurred? Demonstration of EC quiescence would help to ensure similar cell cycle states. The definition of "Notch-positive" and "Notch-negative" cells is a bit misleading, as NICD levels and localization are a better indication of canonical Notch activation, and not the presence or absence of Notch protein(s). Further, NICD activation is also dependent on the levels of Notch ligands, which was not addressed. Are the authors able to confirm "OFF", "Low", "High", and "ON" classifications based on NICD intensity and localization with downstream Notch gene activation at a single-cell level? Or correlation between NICD status and the phase of cell cycle or proliferation status?
R: We thank this reviewer for the comment. Overall, NICD either nuclear or cytoplasmic can give a measure of how much a cell is relaying canonical notch signalling in a small timescale (minutes, which is also the timescale affected by lateral inhibition, Sjoqvist M and Andersson ER, Dev Biol, 2019). By evaluating single cells in the context of their population in multiple fields of view and samples we can get an indication of how frequently a particular cell type tends to actively transduce canonical NOTCH (under confluent conditions). As this and other reviewers have pointed out NOTCH signal transduction mediated by NICD can be affected by several factors limiting the potential to infer actual activation of the pathway (i.e., downstream gene transcription. As suggested by this and other reviewers we are including measures of downstream gene activation, in particular we have included HES1 staining in our workflow, and we will include these data in a new analysis (also see response to R1 point 3). We will also provide new metrics of spatial autocorrelation to evaluate the tendency to lateral inhibition (R1 point 3) and correlation between parameters using continuous mesures and therefore we will remove the previous classification based on thresholds. Finally, we are performing a qRT-PCR screening to assess baseline levels of DLL4, NOTCH1 and JAG1 which we will present as supplementary material.
Do as I say, Not(ch) as I do: Lateral control of cell fate
Sjoqvist M and Andersson ER, Dev Biol, 2019
PMID: 28969930
The existing workflow/platform is adapted for images obtained from the Operetta CLS system (Perkin Elmer) and Harmony software (proprietary), which may not be available for broader users in the EC field. It would be helpful to include ImageJ macros for the bulk automatic import of TIFF, renaming and upscaling of resolution/bit quality to match the formats that are compatible with the software.
R: We thank this reviewer for the comment. We have now included an ImageJ macro (available in the GitHub repository) which in principle can import and elaborate images from any source. We didn’t include a specific option in our current user interface because the relabelling operates by parsing original filenames into fields which are then renamed according to user input and each HT platform adopt different regular expression to encode filename. Any user with a basic literacy in ImageJ macro scripting can achieve relabelling and elaboration of their own file given that their filenames use regular expressions which can be parsed. Also, it is relatively easy (again by modifying the macro) to include user defined pre-processing steps including image scaling. An example of parsing method for Operetta CLS filenames is provided in appendix 1.
Could the authors comment on the manpower (hours from start to finish for experiments, staining, imaging, analysis, etc.) and cost of the ECPT pipeline relative to emerging single cell technologies such as single cell-RNA sequencing.
Further, one major advantage of imaging technologies is the ability to assess live cell dynamics, which are particularly relevant in response to stimuli and agonists. Have the authors utilized the ECPT platform for these approaches, in particular, to assess the differential EC subtype dynamics in proliferative conditions?
R: In terms of manpower the workflow is not very demanding. Our current dataset is based on images extracted form 4 independent experiments (18 wells each). The process is sequential, therefore a single user trained in cell biology, automated microscopy and in the use of the different ECPT components (ImageJ, CP, CPA and R) could perform the experiment alone. The timing of each experiment will depend on circumstantial factors, however once the ECPT is trained for specific user’s requirements (which can require some trials and errors depending on user’s experience) the whole process from cell fixation and staining, through image acquisition (~2 h acquisition for each experiment on an Operetta CLS system), to dataset build-up can take less than one week. For example, elaborating the current image database (~6000 images for four fluorescence channels) which data are presented throughout, had the following raw elaboration times on a Mac Book Pro 2017 equipped with an intel i7 processor and 16 Gb of RAM:
- Image pre-processing and relabelling ~1h
- Generation of probability maps for VEC and NICD ~3h
- CP pipeline run (Cell segmentation, objects measurements and classification) ~16h
- Data import (R studio) ~20m
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We will measure these parameters more precisely in the new experimental run and present timings for each step in a new table in appendix 1.
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After main dataset is created R studio can perform most statistical analyses and data plotting almost instantly.
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We fully appreciate the value of employing ECPT in live imaging setups and we believe it is one of the most promising future applications. We didn’t address live microscopy experiments in the context of ECPT development and validation presented in the current manuscript therefore we cannot present example data or proof of concept. However, we can confidently comment that time lapse experiment would not endow further layers of complexity in terms of image analysis workflow. Therefore, given appropriate set of live markers (e.g., transgenic fluorescently tagged CDH5 for EC segmentation and junctions analysis) we believe that the current implementation of ECPT is already fully equipped to facilitate elaboration and analysis of imaging data derived from time lapse experiments.
The authors should discuss the ability to amend or revise of the ECPT platform to incorporate analysis of additional markers that may be obtained through imaging, and discuss greater implications and utility to specifically tailor the workflow for other researchers in vascular biology, or to other monolayer culture systems. Further, they should better highlight the novel observations obtained with the ECPT compared to traditional methodology.
R: We thank this reviewer for the comments. We will provide evidence of ECPT flexibility within this manuscript by including, during the time of this review process, a new analysis for downstream NOCTH signalling (HES1). We will move analysis of cell “activation” (i.e., stress fibres analysis) to supplementary information and include a more through discussion of how automated single cell classification could improve content, speed, reliability and robustness of quantification tasks which are currently exposed to long and tedious processing times and conscious/unconscious observer biases.
**MINOR COMMENTS:**
We thank this reviewer for the very thorough revision of the manuscript. It is truly invaluable to us to improve it. Below responses to specific technical points, we will fix all stylistic, formatting and typographical issues in revised version of the manuscript.
- There are minor typographical, capitalization and grammatical errors throughout.
R1: Thanks, we will fix these in updated version of the manuscript.
Why was fibronectin used to coat plates, and what was rationale for using this ECM substrate versus gelatin (most commonly used in EC cultures) or type I collagen?
R2: We used fibronectin for immunostaining experiments similar to what reported in our previous work (Veschini et al, 2007, 2011, Wiseman et al, 2019) and also in Andriopoulou P et al,1999. In general, in our experience FN gives better cell adhesion in comparison to gelatin when culturing EC on glass or other substrates different from cell culture plastic. FN is the cell culture substrate recommended by Promocell therefore, we also used FN for cell expansion to avoid any phenotypic change which might have been caused by switch in cell culture substrate.
3. Based on the various box plots present throughout the figures, it appears that some parameters have a large range of values. Is it possible or helpful to set minimum and maximum exclusionary criteria? Further, in the way that these data are presented, it is difficult to appreciate the effects of a treatment such as 48h of VEGF, as the magnitude of STB Index difference, for example, appears small, and it is difficult to understand whether these significant differences are biologically relevant, as assessed.
R3: We agree that in absence of exclusion criteria it is difficult to infer biologic meaning out of subtle differences (e.g., the tiny difference in STB index between HAoEC in presence or absence of VEGF). In the current version of the manuscript, we attempted to be agnostic in regards whether some observed small but significant mean differences could endow biologic meaning and discussed larger variation as biologically meaningful, for example the differences in STB index among cell types. We argue that tiny differences in the distribution of some selected parameter across experimental conditions could reflect underlying mechanisms masked by biologic noise, therefore catching a glimpse of these variations via ECPT could inspire novel experiments to specifically address their full biologic significance.
To the interest of better understanding of the current manuscript we will re elaborate our data to provide more immediate metrics and highlight outstanding features.
Use of arrows and further description in Figure 1 would help the reader understand what specific features are different in the various EC subtypes. As well, the representative micrographs for HPMEC appear blurry compared to other panels (Fig. 1).
In Figure 2, the panels in A, B and C do not correspond horizontally, and it may be cleared to demonstrate "Segmentation & features extraction" overlays from the same representative micrographs shown in panel A. Labeling of the individual panels and software used for panel B would help the readership understand what is being quantified and how. The second panel in "C" appears blurry.
In Figure 3, labelling the color code for quiescent, activated and stressed categories on graphs and in legend would be helpful to easily identify populations.
R4-6: Thanks, we will fix these in updated version of the manuscript.
For Figure 4, line separators or more obvious grouping to distinguish discontinuous, linear and stabilized junction types in panel A. What proportion of the different EC subtypes contains discontinuous, linear and stabilized junctions at confluence/quiescence? Is there a correlation between discontinuous junctions and proliferating cells?
R7: We will perform new analyses to address correlation between proliferation and junctions and proliferation vs HES1. We will restructure data presentation on junctions to display different proportion of junctions per cell or per cell type rather than a unified value (STB index).
It would be useful to distinguish the effects of published mediators on junctional integrity in intact EC monolayers (i.e. histamine; VEGF) from those shown in this automated quantitation. It appears that 50 ng/mL of VEGF treatment for 48h only slightly increases STB index based on panel C.
R7c__: __We agree that increase of STB index in HAoEC and HPMEC upon VEGF treatment might not be highly biologically meaningful, save consideration in point 3 above. However, difference in HUVEC (+- VEGF) is visually appreciable in images (i.e., VEGF treated HUVEC seem to have more linear junctions) therefore we believe that the ~16 units difference in STB index is biologically meaningful. As discussed in point 7 above, we will restructure data presentation to better clarify these aspects.
Figure 5 panel B should provide legend in graphs/figures or figure legends to highlight the color-coding matching the OFF, Low, High and ON groups. Further, it is unclear the difference between "High" and "ON" groups. The authors state that "thresholds were selected empirically", however, it is unclear whether this was derived through utilization of known Notch activators or inhibitors, and how this relates to the threshold of Notch activity necessary to enhance proliferation or maintain quiescence. In Supplementary Figure 4 (which I believe is mislabelled as Supplementary Figure 5), shows only a weak positive correlation between nuclear NICD intensity and mean STB index. It would be of interest to see the plot from Supplementary Figure 5 for each of the EC subtypes, in the presence and absence of VEGF. As well, for Figure 5, on C and D panels, it would improve clarity to revise "Low" and "High" descriptors with "Low NICD activity" and "High NICD activity".
R8: As discussed above we will revise our analyses to remove NOTCH categories and instead show spatial autocorrelation analyses which work on continuous data.
In Supplementary Table 1, "Widt/length" should be "Width/length"
R9: Thanks, we will fix this in updated version of the manuscript.
For Supplementary Figure 3, it would be of use to show DNA distribution intensities from proliferating, non-confluent EC subtypes to demonstrate the validity of this methodology to identify cells in G0/G1, S and G2/M phases, as highlighted in panel A. Could the authors comment on the discrepancy between the percentage of cells identified as quiescent by ECPT and the percentage of cells in G0/G1? The comment that "VEGF induced a small detectable increase in proliferation rate in all EC" is curious, as a dose of 50 ng/mL of VEGF should be a relatively strong stimulator of proliferation/migration in ECs.
R10: We will perform ECPT analysis on sub-confluent or sparse cells to further validate our analysis. Qualitative data on preliminary images seems to confirm that the proliferation rate in sparse cells is very high (>70%). To perform the evaluation we followed and improved a previously published method (Roukos et al, Nat Prot, 2015)
Regarding the relation between cell in G0/G1 and assessment of “quiescent” phenotype (which nomenclature will be revised as discussed above), it is important to highlight that we reported data on stress fibres analysis (i.e., classification into “quiescent”, “activated” and “stressed” cells) only on the cells in G0/G1 (i.e., we excluded proliferating cells from this analysis as we assumed that all proliferating cells would be “not quiescent” and bias our estimation).
For Supplementary Figure 5, "Nuclear NOTCH intensity" on the Y-axis should read "Nuclear NICD intensity", as it does not appear that Notch was stained. It would also be of benefit to overlay the ranges for "OFF, Low, High and "ON" to appreciate ranges of activation. Is there any correlation between NICD nuclear intensity and proliferative index?
R11: We will present correlation between NICD or HES1 and proliferation in revised version of the manuscript.
Definitions should be provided for many terms. i.e. vascular endothelial-cadherin (VE-CAD; CDH5); HUVEC (human umbilical vein endothelial cell); HAoEC (human aortic endothelial cell); HDMEC (human dermal microvascular endothelial cell); NICD (NOTCH intracellular domain); VEGF (vascular endothelial growth factor); etc. at first appearance.
R12: We will add this information in revised version of the manuscript.
For EC subtypes purchased from commercial vendor, it would be of interest to understand how many unique donors these cells/data were derived from, and whether there are any differences in basic donor information such as age, sex, etc. Further, Promocell catalogs proliferative rate for each of their lot numbers, and it would be of interest how this compares to the values determined using the ECPT software analysis package.
R13: We will add this information in revised version of the manuscript.
1 In the "Cell culture" section of the methods, HDMEC from Promocell are listed, however, the manuscript and figures show data from HPMEC. Both EC subtypes are available from Promocell, however, HDMEC are from dermal origin.
1 Vascular endothelial-cadherin should be abbreviated "VE-CAD" or "CDH5" and not "VEC", as this is not a standard or gene notation, and will likely be confused with the more common abbreviations for venous or vascular EC. It seems as though "CDH5" is used most commonly throughout manuscript, so this should be used throughout.
1 The authors refer to "activated NOTCH" when describing antibodies in the methods, however, it would be clearer to the reader to simply refer to the antibody target (NICD), and mention that this reflects canonical NOTCH downstream activation.
The sentence in the "Immunostaining" methods "CDH5 is a lineage marker..." should be moved to results/discussion as these details are out of place in methods.
How were the 3 areas captured per wells designated? Were these locations the automated, and the same for all wells?
"Appendix - Figure" notation should be revised to "Appendix Figure" for consistency and to avoid confusion.
R14-19: Thanks, we will fix these in updated version of the manuscript.
How were artifacts and mis-segmented cell objects excluded?
R20: We will add this information in the revised appendix. As general rules, cells containing NaNs values in any of the parameters, cells fragments or merged cells (evaluated using area measurements) and cells with no detectable junctions were all excluded (total cell excluded from analysis were ~ 2.5 % of the initial dataset).
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In "Statistical analysis" "Tuckey's" should be "Tukey's". "HSD" should be defined "honestly significant difference" or simply removed, as Tukey's is most common name.
In "Statistical analysis", "significative" should be "significant" or "statistically significant".
Scale bars should be added to micrographs.
R21-23: Thanks, we will fix these in updated version of the manuscript.
Could the authors comment on the necessity of µclear plates, which substantially increases the cost per plate/experiment.
R24: m**clear plates were used to allow image acquisition with a 40x water immersion objective in the Operetta CLS (impossible with standard 96 well plates). Cell grown on coverslips and mounted on microscopy slides could be used as well with significant increase in acquisition time (Wiseman et al, 2019).
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Were other seeding densities and times investigated?
R25: We will evaluate sparse cells in revised version of the manuscript as discussed above.
More description on potentially novel observations between these three primary EC subtypes would be informative for the readership to appreciate
The references do not appear in chronological order. Further, consistency of reference formatting should be reviewed, and appropriate journal name abbreviations should be used.
R26-27: Thanks, we will fix these in updated version of the manuscript.
Reviewer #3 (Significance (Required)):
- This manuscript presents a conceptual and technical advance, introducing a high throughput imaging platform to assess endothelial phenotypes
- Within the field of angiogenesis, several tools exist, either proprietary, or leveraging ImageJ software to assist in assessment of cells. The ECPT provides a more complex analysis platform to integrate analysis of multiple endpoints
- This work would be of interest to vascular biology laboratories to adopt a more comprehensive view of heterogeneous endothelial phenotypes in vitro
- As a vascular biology researcher, I have had extensive experience with in vitro culture of various endothelial cell subtypes from human and mouse. My field of expertise gives me the perspective of the nuances of the direct handling and phenotyping of ECs, and have worked specifically worked with HUVEC, HAoEC and HPMEC, and assessed the impact of key factors relevant in angiogenesis such as VEGF, Notch and other mediators.
R: We thank the reviewer for the very appreciative comments, and we hope that with the revised version of the manuscript we will be able to fully address remaining concerns.
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Referee #3
Evidence, reproducibility and clarity
SUMMARY:
The manuscript by Chesnais et al. presents a novel endothelial cell (EC) profiling tool (ECPT) which provides spatial and phenotypic information from individual ECs, and was tested with a variety of specialized EC subtypes (arterial, venous, microvascular). They present a high throughput immunostaining and imaging-based platform using culture of human ECs on 96-well plates and capture of fixed, stained samples on a Perkin Elmer Operetta CLS system. The authors report the use of this ECPT tool to investigate EC phenotypes from human umbilical vein ECs (HUVEC), human aortic ECs (HAoEC) and human pulmonary microvascular (HPMEC) in relation to 50 ng/mL VEGF stimulation for 48 hours, and the general parameters of proliferation, Notch activation and stress fiber rearrangement (F-actin), and present this as a prospective platform to examine differences in EC phenotypes and responses at a more individualized level.
MAJOR COMMENTS:
- Fundamentally, the advantage of single cell technologies is the ability to segregate populations to make novel observations. One area that would be of interest to explore in this manuscript using this ECPT platform would be reporting the results from single cell analysis that is then subsequently pooled within a sub-population, rather than sub-stratifying populations to reflect the multiple phenotypes that may be present within a single "confluent" well. With analysis of EC heterogeneity, it would be of interest to differentiate heterogeneity within EC subtypes at the culture/treatment conditions presented, and heterogeneity between EC subtypes.
- The term "stable IEJ" is used and refers to 48h after seeding 40,000 cells on a 96-well plate, but it is unclear how the authors defined or demonstrated a "stable" junction. In previous reports, longer-term culturing of EC monolayers well beyond the point of confluence has been shown to result in junctional complex rearrangement (Andriopoulou P et al. Arterioscler Thromb Vasc Biol. 1999; reviewed in Bazzoni G & Dejana E. Physiol Rev. 2004). To this point, the fact that the different EC subtypes investigated had different percentages of "quiescent cells" suggests that the monolayers were not completely quiescent. The statement that the IEJ classification is "an immediate index of EC activation in contrast to quiescence" should be further supported by references or data. The definition of quiescent EC as simply non-proliferating, non-migrating is somewhat reductionist, and oversimplifies EC states. The authors state that HAoEC and HUVEC "...appeared more active...", but it is unclear what "active" means, and whether this may simply reflect that these cells had not yet reached confluence or quiescence in the 48h total culture time. As well, it is unclear how "migratory phenotypes" could occur in confluent monolayers. It would be helpful to see the data for these observations. If leaving ECs longer in culture, are the authors able to achieve a higher percentage of quiescent cells?
- Could the authors comment on the baseline NICD immunoreactivity in the nuclei in HAoEC and HPMEC compared to HUVEC? Is this a reflection of active NOTCH signaling? Or rather, is it possible contact-inhibition (and downregulation of NOTCH) may not have occurred? Demonstration of EC quiescence would help to ensure similar cell cycle states. The definition of "Notch-positive" and "Notch-negative" cells is a bit misleading, as NICD levels and localization are a better indication of canonical Notch activation, and not the presence or absence of Notch protein(s). Further, NICD activation is also dependent on the levels of Notch ligands, which was not addressed. Are the authors able to confirm "OFF", "Low", "High", and "ON" classifications based on NICD intensity and localization with downstream Notch gene activation at a single-cell level? Or correlation between NICD status and the phase of cell cycle or proliferation status?
- The existing workflow/platform is adapted for images obtained from the Operetta CLS system (Perkin Elmer) and Harmony software (proprietary), which may not be available for broader users in the EC field. It would be helpful to include ImageJ macros for the bulk automatic import of TIFF, renaming and upscaling of resolution/bit quality to match the formats that are compatible with the software.
- Could the authors comment on the manpower (hours from start to finish for experiments, staining, imaging, analysis, etc.) and cost of the ECPT pipeline relative to emerging single cell technologies such as single cell-RNA sequencing. Further, one major advantage of imaging technologies is the ability to assess live cell dynamics, which are particularly relevant in response to stimuli and agonists. Have the authors utilized the ECPT platform for these approaches, in particular, to assess the differential EC subtype dynamics in proliferative conditions?
- The authors should discuss the ability to amend or revise of the ECPT platform to incorporate analysis of additional markers that may be obtained through imaging, and discuss greater implications and utility to specifically tailor the workflow for other researchers in vascular biology, or to other monolayer culture systems. Further, they should better highlight the novel observations obtained with the ECPT compared to traditional methodology.
MINOR COMMENTS:
- There are minor typographical, capitalization and grammatical errors throughout.
- Why was fibronectin used to coat plates, and what was rationale for using this ECM substrate versus gelatin (most commonly used in EC cultures) or type I collagen?
- Based on the various box plots present throughout the figures, it appears that some parameters have a large range of values. Is it possible or helpful to set minimum and maximum exclusionary criteria? Further, in the way that these data are presented, it is difficult to appreciate the effects of a treatment such as 48h of VEGF, as the magnitude of STB Index difference, for example, appears small, and it is difficult to understand whether these significant differences are biologically relevant, as assessed.
- Use of arrows and further description in Figure 1 would help the reader understand what specific features are different in the various EC subtypes. As well, the representative micrographs for HPMEC appear blurry compared to other panels (Fig. 1).
- In Figure 2, the panels in A, B and C do not correspond horizontally, and it may be cleared to demonstrate "Segmentation & features extraction" overlays from the same representative micrographs shown in panel A. Labeling of the individual panels and software used for panel B would help the readership understand what is being quantified and how. The second panel in "C" appears blurry.
- In Figure 3, labelling the color code for quiescent, activated and stressed categories on graphs and in legend would be helpful to easily identify populations.
- For Figure 4, line separators or more obvious grouping to distinguish discontinuous, linear and stabilized junction types in panel A. What proportion of the different EC subtypes contains discontinuous, linear and stabilized junctions at confluence/quiescence? Is there a correlation between discontinuous junctions and proliferating cells? It would be useful to distinguish the effects of published mediators on junctional integrity in intact EC monolayers (i.e. histamine; VEGF) from those shown in this automated quantitation. It appears that 50 ng/mL of VEGF treatment for 48h only slightly increases STB index based on panel C.
- Figure 5 panel B should provide legend in graphs/figures or figure legends to highlight the color-coding matching the OFF, Low, High and ON groups. Further, it is unclear the difference between "High" and "ON" groups. The authors state that "thresholds were selected empirically", however, it is unclear whether this was derived through utilization of known Notch activators or inhibitors, and how this relates to the threshold of Notch activity necessary to enhance proliferation or maintain quiescence. In Supplementary Figure 4 (which I believe is mislabelled as Supplementary Figure 5), shows only a weak positive correlation between nuclear NICD intensity and mean STB index. It would be of interest to see the plot from Supplementary Figure 5 for each of the EC subtypes, in the presence and absence of VEGF. As well, for Figure 5, on C and D panels, it would improve clarity to revise "Low" and "High" descriptors with "Low NICD activity" and "High NICD activity".
- In Supplementary Table 1, "Widt/length" should be "Width/length"
- For Supplementary Figure 3, it would be of use to show DNA distribution intensities from proliferating, non-confluent EC subtypes to demonstrate the validity of this methodology to identify cells in G0/G1, S and G2/M phases, as highlighted in panel A. Could the authors comment on the discrepancy between the percentage of cells identified as quiescent by ECPT and the percentage of cells in G0/G1? The comment that "VEGF induced a small detectable increase in proliferation rate in all EC" is curious, as a dose of 50 ng/mL of VEGF should be a relatively strong stimulator of proliferation/migration in ECs.
- For Supplementary Figure 5, "Nuclear NOTCH intensity" on the Y-axis should read "Nuclear NICD intensity", as it does not appear that Notch was stained. It would also be of benefit to overlay the ranges for "OFF, Low, High and "ON" to appreciate ranges of activation. Is there any correlation between NICD nuclear intensity and proliferative index?
- Definitions should be provided for many terms. i.e. vascular endothelial-cadherin (VE-CAD; CDH5); HUVEC (human umbilical vein endothelial cell); HAoEC (human aortic endothelial cell); HDMEC (human dermal microvascular endothelial cell); NICD (NOTCH intracellular domain); VEGF (vascular endothelial growth factor); etc. at first appearance.
- For EC subtypes purchased from commercial vendor, it would be of interest to understand how many unique donors these cells/data were derived from, and whether there are any differences in basic donor information such as age, sex, etc. Further, Promocell catalogs proliferative rate for each of their lot numbers, and it would be of interest how this compares to the values determined using the ECPT software analysis package.
- In the "Cell culture" section of the methods, HDMEC from Promocell are listed, however, the manuscript and figures show data from HPMEC. Both EC subtypes are available from Promocell, however, HDMEC are from dermal origin.
- Vascular endothelial-cadherin should be abbreviated "VE-CAD" or "CDH5" and not "VEC", as this is not a standard or gene notation, and will likely be confused with the more common abbreviations for venous or vascular EC. It seems as though "CDH5" is used most commonly throughout manuscript, so this should be used throughout.
- The authors refer to "activated NOTCH" when describing antibodies in the methods, however, it would be clearer to the reader to simply refer to the antibody target (NICD), and mention that this reflects canonical NOTCH downstream activation.
- The sentence in the "Immunostaining" methods "CDH5 is a lineage marker..." should be moved to results/discussion as these details are out of place in methods.
- How were the 3 areas captured per wells designated? Were these locations the automated, and the same for all wells?
- "Appendix - Figure" notation should be revised to "Appendix Figure" for consistency and to avoid confusion.
- How were artifacts and mis-segmented cell objects excluded?
- In "Statistical analysis" "Tuckey's" should be "Tukey's". "HSD" should be defined "honestly significant difference" or simply removed, as Tukey's is most common name.
- In "Statistical analysis", "significative" should be "significant" or "statistically significant".
- Scale bars should be added to micrographs.
- Could the authors comment on the necessity of µclear plates, which substantially increases the cost per plate/experiment.
- Were other seeding densities and times investigated?
- More description on potentially novel observations between these three primary EC subtypes would be informative for the readership to appreciate
- The references do not appear in chronological order. Further, consistency of reference formatting should be reviewed, and appropriate journal name abbreviations should be used.
Significance
- This manuscript presents a conceptual and technical advance, introducing a high throughput imaging platform to assess endothelial phenotypes
- Within the field of angiogenesis, several tools exist, either proprietary, or leveraging ImageJ software to assist in assessment of cells. The ECPT provides a more complex analysis platform to integrate analysis of multiple endpoints
- This work would be of interest to vascular biology laboratories to adopt a more comprehensive view of heterogeneous endothelial phenotypes in vitro
- As a vascular biology researcher, I have had extensive experience with in vitro culture of various endothelial cell subtypes from human and mouse. My field of expertise gives me the perspective of the nuances of the direct handling and phenotyping of ECs, and have worked specifically worked with HUVEC, HAoEC and HPMEC, and assessed the impact of key factors relevant in angiogenesis such as VEGF, Notch and other mediators.
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Referee #2
Evidence, reproducibility and clarity
The manuscript by Chesnais et al reports development of workflow for analysis of cultured endothelial cells , which they call Endothelial Cell Profiling tool (ECPT). Using ECPT they analyse several parameters in three different endothelial cell types (HuAEC, HUVEC and HPMEC), such as cell morphology, activation of cytoskeleton, VE-cadherin junctions, cell proliferation and Notch activation, under steady conditions and upon treatment with VEGF. The analysis allows to observe some predicted changes, such as increase in cell cycle and junctional activation in cells treated with VEGF-A, and such changes are highly heterogeneous. Overall, this is a potentially useful albeit not revolutionary tool for batch analysis of cultured endothelial cell phenotypes.
I have the following comments:
- To make their case the authors should provide a comparison with other currently used approaches for EC phenotypic analysis in vitro - what is the advantage of using ECPT? The authors repeatedly use the term "single-cell level of analysis ", but this is in fact the case of any IF based analysis of cultured cells.
- I strongly recommend to stain HPMECs for PROX1, these cells are frequently 100% lymphatic endothelial cells. In this case the authors compare different lineages and not blood endothelial cells from different locations.
- Please provide evidence for specificity of NICD antibody.
- Figure 1: HPMEC picture appears out of focus
- Figure 3 A - it is not entirely clear what is the difference between activated and stressed phenotype, they look quite similar.
- Figure 5 - what is the difference in NICD localization between "high" and "On" conditions?
- Since the authors make a correlation between Notch activity and junctional stabilization, it would be important to confirm this by other means, such as analysis of Notch target genes.
Technical and minor
- Methods mentions HDMECs (human dermal microvascular endothelial cells) but the authors discuss HPMEC throughout the text
- Please add scale bars on all microscopy pictures.
- Please provide the information on what isoform of VEGF-A was used for stimulation and the rationale for selecting the concentration.
Significance
The authors provide a workflow for the phenotypic analysis of cultured cells. Such tool is potentially useful, although the examples the authors show do not reveal striking examples of why such analysis is better in comparison to existing approaches. My guess is that the analysis may be faster and less tedious, once the training sets are generated, but this is not specified. My speciality is endothelial cells biology.
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Referee #1
Evidence, reproducibility and clarity
The authors highlight the importance of endothelial heterogeneity using endothelial cells from different tissues. They examined aortic and pulmonary endothelium as well as HUVECs. They cultured the cells in identical conditions and also stimulated them with a physiological concentration of vascular endothelial growth factor as well high concentrations as would be found in cancers. They developed a profiling tool that allowed analysis of individual endothelial cells within a monolayer and quantification of inter-endothelial junctions, Notch activation, proliferation and other features.
Major comments
- It would be useful to apply this technology one step beyond two-dimensional culture, to use vessels opened up longitudinally so that one can see the monolayer of endothelial cells and assess whether it is relevant in primary material in situ. I think this would be a major utility of the whole approach.
- There are some very nice images here but disappointed not see a field that could show staining and markers for several of the target proteins and thus show the heterogeneity and randomness or organisation of the endothelial cells. For example are any clusters of a subtype of endothelial cells around proliferating cells.
- The Notch signalling is an important aspect of this work, particularly evidence of lateral inhibition would have been of value. For example, one might expect cells adjacent to each other to have alternating high and low NICD. NICD staining alone does score the extent of the signalling because of many factors that can influence the transport of the cleaved NICD. Really a marker of Notch signalling downstream e.g. HES or HEY family ,DLL4 fis needed to give more information about this critical aspect.
- I really do not think that in Figure 5 it is justified to have a red line drawn through the cloud of points. The correlation coefficient is so low that this is meaningless. The failure to distinguish a P value from biological relevant is worrying. Much better comparison would have been between NICD staining and a downstream gene regulated by notch.
- It is important to know that the antibodies used for staining have be validated by the investigators. They would need to show a single band on Western blots or be able to block staining on immunohistochemistry. We all know the manufacturers can be unreliable and use high concentrations of proteins for Western blots. These should be added as a supplementary figure.
Significance
This represents a valuable and thorough methodology likely to be highly useful to many groups and show new insights into endothelial biology.
Wide audience, cancer, cardiology, vascular disease-covid.
My expertise >100 papers on angiogenis in cancer, basic mechanism, therapy models, bioinformatics IHC, patients, clinical trial. H score 190 Google Scholar
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Reply to the reviewers
Point-by-point response, comments in (blue), our response in (black)
Note: we included 6 Figures in our response, yet the ReviewCommons system does not appear to support including images as part of the response. These Figures are in the original "Initial Response" file available to ReviewCommons. We requested that Review Commons post our "Initial Response" file that contains these figures so that this information is available.
Reviewer #1
*In the paper by Gowthaman et al., the authors aim at better understanding the molecular mechanisms controlling divergent non-coding transcription (DNC). They describe a high-throughput yeast genetic screen using two strains in which two loci consisting of a coding and a divergent non-coding transcription unit (CGC1-SUT098 or ORC2-SUT014) were replaced by a bidirectional fluorescent reporter construct encoding mCherry in the coding direction and YFP in the non-coding direction. The two reporter strains were crossed with the yeast deletion library and mutants leading to increased or decreased YFP signal were selected as potential DNC repressors or activators. The two screens identified a number of common potential repressors and activators. Components of the Hda1C histone deacetylase complex were identified as DNC repressors in both screens. This phenomenon was confirmed genome-wide by performing NET-Seq in WT as well as hda1D and hda3D strains. This experiment allowed to identify 1517 DNC transcripts repressed by Hda1. Further analyses indicate that Hda1C represses DNC genome-wide independently of expression levels and that loss of Hda1 does not substantially affect coding transcription.
Live-cell imaging of transcription was then used to show that loss of Hda1 increases DNC transcription frequency rather than duration providing novel information on the link between DNC transcription initiation kinetics and chromatin regulation. Finally, using Chip-seq, the authors show that the level of acetylation over the divergent non-coding units is increased in the absence of Hda1 and some experiments suggest that H3K56 acetylation also contributes to DNC regulation, further strengthening the importance of elevated histone acetylation in efficient DNC.
Importantly, several components of the SWI/SNF chromatin remodeling complex were identified as activators confirming earlier observations (Marquardt et al., 2014). SAGA subunits were also among potential DNC activators, however these effects could not be confirmed through validation experiments. The authors conclude that DNC may be independent of specific activators and mainly due to transcriptional noise resulting from the adjacent NDR.
Overall this paper is very well structured, clearly written and the experiments are well controlled. The genetic screen identifies novel factors involved in the regulation of DNC. The study clearly demonstrates that the level of acetylation is a key regulator of divergent non-coding transcription and that histone deacetylation by Hda1 reduces the frequency of DNC initiation events. While this conclusion is strongly supported by the Net-Seq and Chip-seq metagene analyses, the fluorescence mCherry and YFP values or qRP-PCR analyses of specific genes do not always behave as expected when looking at absolute values rather than mCherry/YFP or GCG1/SUT098 ratios, which is sometimes disturbing when reading the paper. Therefore, the following points should be clarified.*
We are grateful for the kind appreciation of our manuscript and clarify the remaining questions in the revised manuscript.
**Major points**
#1.1: Figures 2 and S2A: Figures 2C and D show the mCherry/YFP fluorescence and GCG1/SUT098 RT-qPCR gene expression ratios respectively, which are consistent with a repressive effect of Hda1C on DNC transcription and a potential DNC activating effect of SAGA components. However, the absolute mCherry and YFP or GCG1 and SUT098 expression values presented in Figures S2A and S2B show the opposite: loss of Hda1C subunits rather leads to a decrease in mCherry with not much effect on YFP; moreover loss of Hda3 results in decreased SUT098, which is inconsistent with the whole model. The same comment is valid for the SAGA mutants. It would be good to provide some explanation for these a priori contradictory observations, especially for the Hda1c mutants, which are the major focus of the study. The Net-Seq analyses are certainly more reliable since less subject to protein or RNA stability effects, which may underlie some of the inconsistencies between protein and RNA absolute levels.
Thank you for this comment. We offer enhanced clarity in the revised manuscript.
In general, transcription in each direction shows a weak yet highly statistically relevant positive correlation (Spearman rho = 0.26, p-value = 4.94e-24). We are enclosing a plot based on NET-seq data that supports the correlation in each direction of a NDR as part of our response below (RFig.1). To unpick relative effects the ratio captures these effects well, in our experience better than the individual fluorescence measurements or RT-qPCR. Of course, we are ultimately interested in transcription and fluorescence measurements or RT-qPCR of steady-state RNA are only an approximation. Resources and time constraints limit how many mutations we can examine by techniques such as NET-seq, which are arguably most informative. The positive correlation between transcription in each direction has the effect that relative differences can manifest themselves through detectable effects of the other fluorophore. As this reviewer mentions, we can be most confident of results that we could further validate by NET-seq or live-cell imaging.
(INSERT Rfig1)
RFig1: Scatterplot of NET-seq data for DNC/host gene pairs. Each point corresponds to a bidirectional gene promoter overlapping with a nucleosome-depleted region (NDR). The values represent NET-seq FPKM values in protein-coding (x-axis) vs non-coding (y-axis) directions. These data support a statistically significant correlation (Spearman test: rho = 0.2554876, p-value = 4.939658e-24).
#1.2: Figure 3: this figure examines the effect of Hda1 and Hda3 on the 1517 DNC transcripts. Does loss of this HDAC also increase the expression of all the other 2219 non-coding transcripts identified by Net-Seq, which would make Hda1C a more general repressor of non-coding transcription?
We have performed the analysis for all other non-coding transcripts in Hda1C mutant NET-seq data and added it as part of this response RFig2. Quantification of CUTs, SUTs and other lncRNAs that are not resulting from DNC in Hda1C mutants results in a slight increase in the nascent transcription that is not statistically significant. These data do not offer strong support for the idea that Hda1C represents a more general repressor. We added this plot as novel supplementary figure S3D and adjusted the text of the revised manuscript (line 214).
(INSERT Rfig2)
RFig2: Metagene plot of NET-seq data for non-coding RNA that are not classified as DNC. Metagene plot shows genomic windows [TSS - 100 bp, TSS + 500 bp] relative to the annotated starts of ncRNA transcripts.
#1.3: Moreover, does loss of Hda1 or Hda3 reveal DNC transcripts that were not detected in wild-type? This may increase even more the number of genes with divergent transcription.
We are grateful for the opportunity to clarify this point. We noticed that the yeast genome shows evidence for much more non-coding transcription than annotated. In this paper, we used TranscriptomeReconstructoR for a data-driven annotation of yeast non-coding transcripts, with an emphasis on the boundaries. See also:__ ( DOI: 10.1186/s12859-021-04208-2 ). The set of non-coding transcripts was for example informed by the previously published NET-seq data on wild-type samples (Churchman et al., 2009; Marquardt et al., 2014; Harlen et al., 2016; Fischl et al., 2017). We have clarified relevant Methods sections to make this point more accessible (line 733). The combination of these NET-seq datasets gives a very good sequencing coverage. The Hda1C mutant NET-seq data does not have a better coverage than this combined reference set, so it would be very hard to find new transcripts without prior evidence in our exhaustive set of combined NET-seq data. However, our Supplementary table S3 contains the fold-change values for all DNC transcripts in mutant compared to wild type. Loci with a high fold-change could arguably be regarded as hda-specific. __
#1.4: Figures S3A, B, C: are the 3 groups of DNCs derepressed to the same extent by loss of Hda1 or Hda3? This is difficult to judge given the differences in y-axis scales. Figures S3D, E: the authors show the Net-Seq snapshots for the GCG1 and ORC2 loci. It would be good to add the quantifications as presented in Figure 3 for YPL172C and YDRr216C.
Thank you for the suggestion. We replaced S3A-C with plots that show the same range of the y-axis in the supplementary figure. Hda1C represses DNC in all three cohorts stratified by DNC expression strength. We also added a quantification boxplot for NET-seq signal in the GCG1 and ORC2 loci in revised S3F-I.
#1.5: Figures S4A, B, C and D are not well explained. What does the y axis frequency correspond to? Is it the % of cells showing a signal? Is the intensity of SUT098 higher because the transcription initiation frequency is higher and therefore the transcription site signal is more intense?
We improved the annotation for the supplementary figure S4. We clarified in the legend that the y-axis frequency represents the percentage of frames recorded for transcription initiation spots (TS). The bars represent transcription intensity in all the frames recorded, with active transcription ‘ON’ and without TS ‘OFF’. The intensity increases with higher initiation rates and thus the intensity of SUT098 transcription initiation is high.
#1.6: Figures S4 A-I should be more specifically cited in the text.
We have cited the figures in the text in the revised version.
#1.7: Figure 5A: it is really unexpected and unclear why the mCherry/YFP in the WTH3/hda1D and WTH3/hda1D/H3K56mut is increasing compared to WTH3, since DNC is supposed to increase. Similar comment for Figure S5C. This should be clarified in the text.
Thank you for pointing this out. We missed to address this in the text. The isogenic control “H3 wild type” carries only one copy of the two genes coding for H3, which has a general effect on transcription. We added data showing this as part of our response (RFig3.), and explained this part more clearly in the revised text (line 263). Essentially, the genetic background of the yeast synthetic histone mutant collection sensitizes for a decreased ratio of mCherry/YFP (RFig3.). This result is also included in table S2, where deletions of the histone genes HHT2 (H3) and HHF2 (H4) are listed as shared repressors in both screens. Hda1C mutations show the increased ratio in the sensitized “H3 wild type” background, but not in backgrounds we tested that contain a wild-type dosage of histone genes.
These data remain valid to support the genetic interaction of hda1D along with the substitution mutants of H3K56.
(INSERT Rfig3)
RFig3. Fluorescence signal values of H3WT and BY4741 strains with GCG1pr FPR. The H3WT affects general transcription of coding transcript and decreases the ratio of mCherry/YFP fluorescence.
#1.8: More generally, as already mentioned above, the fluorescence data are expressed either as mCherry/YFP ratio or as absolute values. It would be good to systematically show the ratios and the absolute values of mCherry and YFP signal; the same for coding and DNC RT-qPCR as well as Net-Seq values when available.
We ensured that the absolute data values for flow cytometry and qPCR have been represented in the supplementary figures S2 and S5. The FPKM values for NET-seq data for individual transcript units are provided in the supplementary table S3.
#1.9: Figures S5A and B are not referred to in the text. It should be mentioned and explained how normalization to H3 affects the levels of acetylated H3 over the NDR.
We now refer to the figures in the main text and explained the rationale for normalization.
#1.10:* p. 12 "Our data thus suggest to extend the transcriptional noise hypothesis with activities limiting DNC transcription to account for genome-wide variation in non-coding transcription".
If DNC is the result of "transcriptional noise", it is surprising that in the case of CGC1-SUT098, the transcription frequency is higher in the non-coding versus the coding direction. Is the SUT098 behaving like the coding unit in this case? The authors should comment on that. *
This is very interesting point. One interpretation of the “transcriptional noise” hypothesis is indeed that non-coding transcription is at low level. We selected loci with high DNC expression, so these loci are somewhat contradictory to this idea a priori. Nevertheless, identifying a biological function of non-coding RNAs is challenging, and it remains to be tested if SUT098 represents particularly “loud noise” or if the high transcription indicates that it carries a yet unknown cellular function. In theory, this screen is suitable to identify factors that may be required to induce DNC, perhaps even specifically. To identify such factors a locus with high DNC is needed to facilitate detection, since our previous screen using the PPT1/SUT129 system had lower SUT expression and failed to identify such mutants systematically. This is important, since a mutation lowering DNC needs to start from a sufficiently high fluorescence signal to distinguish it from background fluorescence. Since the results presented did not clearly uncover such factors, we favor the hypothesis of DNC arising due to the promoter architecture at NDRs, see also positive correlation plot in RFig1. The many repressive pathways are also acting on highly expressed DNCs, which is certainly an interesting information provided by this manuscript.
**Minor comments**
#1.11: p. 4 should one talk about Hda1C-linked histone acetylation facilitates... (should be deacetylation...??)
Done.
#1.12: The authors should explain why they chose two coding/non-coding pairs that are cac2D insensitive and whether other criteria, such as level of DNC transcription, were also considered, since GCG1-SUT098 represents one of the most highly expressed divergent non-coding transcripts.
The GCG1 and ORC2 loci were chosen based on i) high DNC levels, ii) a low fold-change of NET-seq data in the cac2∆ and iii) a DNC region free from other transcriptional units. However, this was based on the state-of-the-art annotation in 2015 when we started this project. Also, when we categorized genes as affected by cac2∆, we used a fold-change expression cut-off that suggested that about a third of DNCs are repressed by CAF-I. It appears that we still underestimated the effect of CAF-I, since our data show that the target regions of our new screens are also affected by CAF-I. DNC expression at these loci is high, which would result in a low fold-change in mutants that further increased DNC here.
#1.13: It is hard to understand why both the H3K56A and H3K56Q mutations lead to increased DNC, a result already presented in the Marquardt et al. 2014 paper. It would be helpful to provide a more extensive explanation or hypothesis.
The H3K56 substitution mutant Q is expected to mimic the acetylation state and A is devoid of post-translational modifications. We observe an increase of signal ratio in the mutants because the H3K56ac is both responsible for incorporation and eviction of -1 nucleosomes (Marquardt et al., 2014). Mutations affecting H3K56 can thus result in less -1 nucleosome density and more DNC through reducing incorporation or enhancing eviction. We have improved the revised text to highlight this. We have clarified this in the text (line 271).
#1.14: What defines the level of DNC repression? How does the level of repression correlate with the level of coding transcription?
We have added RFig.1 to address the question about correlation. There is a statistically significant positive correlation between transcription in each direction by NET-seq data in wild type samples genome-wide. However, the correlation is weak (rho = 0.26), which is consistent with locus-specific adjustments of transcriptional strength in each direction. For DNC, several chromatin-based pathways contribute to repression. The resulting level of DNC transcription thus reflects the combined action of several pathways. Here, we characterize Hda1C as a novel player with a genome-wide effect on this phenomenon. Elucidating the mechanistic interplay at specific target DNC loci will be an exciting future research question.
Reviewer #1 (Significance (Required)):
This is a very interesting and innovative study using cutting edge genetic approaches, genome-wide sequencing as well as single cell imaging to extend our understanding of non-coding transcription regulation and its potential impact on gene expression. It is a nice continuation and complement of an earlier study from the same author (Marquardt et al., 2014) and will certainly be of interest to a large chromatin biology audience.
We are grateful for the appreciation of our research on this topic.
Reviewer #2
Promotors are frequently transcribed in both directions. The divergent, \upstream' transcript is frequently unstable. Transcription initiation is regulated through the acetylation of promoter-proximal nucleosomes, where HDAC-dependent deacetylation of histones typically represses transcription initiation.*
*The current manuscript addresses the question whether initiation of coding and divergent, non-coding (DNC) transcription is regulated by the same factors. Previously Marquardt and others showed that H3K56ac-mediated histone exchange has a differential effect on coding and DNC transcription.
Using a clever reporter system, the authors screened for positive and negative regulators that preferentially affect DNC transcription. They discover the Hda1 deacetylase complex as a DNC-biased repressor and diverse HATs as DNC-biased activators. The role of activators could not be validated, presumably due to high variability of the system.*
Focusing on Hda1c the authors present data suggesting a larger effect of Hda1c on 'upstream' nucleosomes associated with DNC transcription than in coding transcription. Genome-wide NET-seq mapping was consistent with this differential regulation. Life cell imaging of one specific case argues that Hda1-mediated repression reduced the time between initiation events. The authors employ state of the art methods and in general the data are of very good quality. The effect size is very small, which raises the broader question whether the results, while statistically significant is biological relevant. I have a few comments that the authors may use to revise their manuscript.
Thank you for the appreciation of our very good data quality. We hope our revision plan will help to clarify some confusion about the scope and effect size.
#2.1) The differentially regulated coding and DNC transcription are defined by a directionality score. The screen was performed with two reporter loci that are strongly biased for DNC transcription (the idea to detect activators did not work out). Considering that coding and DNC transcription may not be totally independent because of the proximity of target nucleosomes, and sense and antisense transcription may compete for regulators, the question arises how levels of coding transcription affect DNC transcription in wildtype and mutants. The authors stratified their results according to levels of DNC transcription, but discussion and data analysis of the effect of coding transcription on the directionality score may be relevant.
We added the plot in RFig.1 above to address the question of correlation between transcription in each direction. NET-seq data supports a weak but highly statistically significant positive correlation between transcription in each direction genome-wide (rho = 0.26, p-value = 4.94e-24). We agree that it is relevant to discuss the effect of coding transcription on the directionality scores and revised the discussion accordingly (line 315). We have used both the coding and DNC signal values to create the comprehensive quadrant scatter plot in Fig. 1D-E. Analysis of mutants along the diagonal illustrates that many mutations affect coding transcription as well as DNC. The directionality score measures deviations from the axis of positive correlation, which requires us to use the information of both fluorophores.
#2.2) The study is strong where the findings can be generalized. The single-molecule live-cell imaging analysis, while done properly, has only limiting impact, because the corresponding coding transcript could not be detected. This si more an anecdotal finding.
There seems to be a misunderstanding, the live-cell imaging measurements of transcription for SUT098 are stand-alone data. SUT098 by itself is a transcription unit, so we measure DNC of this unit independently from GCG1 that has much lower expression. The measurements are specific to SUT098 transcription and the quantification provides new information about the mechanisms involved in the regulation of DNC. We clarified the text in this regard (line 233).
#2.3) The effect size is small (20%, on average) and the variability is high. The fact that the HATs that emerged as very robust activators of DNC transcription could not be validated and that the Hda2 subunit of the HDAC complex was not found statistically significant show the limitations of the study. To their credit, the authors discuss these limitations appropriately.
We have worked on the Methods in the revised manuscript to clarify this confusion (line 712). For the screen, the median signal values represent data from up to 50,000 individual cells. These experiments are remarkably accurate and highly reproducible, especially for molecular biology where n=3 is common. We have uploaded these data to the FlowCore public repository. We encourage any colleague to exploit the opportunity to analyze these data independently to experience the high data quality. With high number of observations, 20% average is a large effect and reflects a rather big shift of the population. As is standard for genetic screens, resource constraints are prohibitive to pursue all hits. In addition, it is expected that only some hits will be affecting transcription of DNC since the fluorescence reporter can be affected by many other cellular events. We focused on the effects on DNC in this manuscript.
There seems to be some misunderstanding, Hda2 is a statistically significant hit in the ORC2/SUT14pr screen; this information is in Fig. 1E. The Hda1C subunits are labeled in purple.
#2.4) Figure S3C suggests that the Hda effect is largest at genes that are poorly expressed, and smaller at more average expression levels. Are we looking at a phenomenon that mainly applies to repressed genes?
Thank you very much for this suggestion. We replaced S3A-C with revised panels where the data is shown with the same y-axis scale, please see also #1.4. We believe the revised presentation also helps to clarify that the mutations increase DNC for all cohorts stratified by DNC expression.
**Minor issues**
#2.5) The NET-seq study involves two replicates. How well did they correlate?
The WT and mutant NET-seq replicates have good correlation (Spearman’s correlation coefficient was above 0.6 for WT and above 0.8 for the mutants).
(INSERT Rfig4)
RFig4. Correlation scatter plot of individual NET-seq replicates of WT, hda1D and hda3D. Spearman correlation coefficients of WT, hda1D and hda3D are 0.677, 0.8 and 0.825, respectively.
#2.6) For the live-cell imaging replicates were not mentioned. Were replicate studies performed?
We have updated the text to make this important point more accessible (line 230). For live-cell imaging studies, transcription is recorded as movies of cells over time. We took multiple movies, and pooled the data from all the cells to improve statistical power. Data from each movie represent individual repeats. We monitored 130 cells on average for the WT and mutant strains over time.
#2.7) Fig 4E is not mentioned in the text (mislabeled as 4D)
Done.
#2.8) Fig S5 is not mentioned in the main text.
__Done.
__Reviewer #2 (Significance (Required)):
In summary, this is a high-quality study that presents the results of a genome-wide screen that will be of interest to colleagues in the narrower field. Due to the small effects the results may appeal less to a general readership.
We are grateful for appreciating our manuscript as a high-quality study. We hope our revisions help to clarify confusion concerning effect size.
Reviewer #3
In this manuscript, Gowthaman et al describe the results and follow up of their screen aimed at identifying regulators of divergent noncoding (DNC) transcription in S. cerevisiae. From this screen, they identify Hda1C as a repressor of DNC transcription, and perform follow experiments to support and detail this finding. In addition to RTqPCR to confirm the reporter and endogenous changes, the authors perform NET-seq to look at global DNC alteration upon Hda1C subunit deletion and identify a number of non-coding transcripts with altered expression levels. In addition, the authors perform live cell imaging to demonstrate that there is a modest restriction of initiation frequency when one of the subunits of Hda1C is deleted. Finally, the authors explore changes to pan-H3 acetylation and the genetic overlap between Hda1C and H3K56ac demonstrating independent genetic pathways, but overall increases in H3 acetylation over DNCs when Hda1C is deleted. Overall, the screen and results are of interest, but the authors overstate some of the conclusions (perhaps most importantly within the title!). I have the following suggestions to improve the manuscript:
Thank you for recognizing the interest in our results. We have revised the manuscript to state the conclusions more cautiously.
**Major comments**
#3.1. The title of the manuscript is based on the single molecule live cell imagining experiments presented in Figure 4. While there is a statistically significant decrease in initiation frequency from deletion of one Hda1C subunit, there is no statistical decrease in deletion of the other two. Furthermore, these experiments were performed at one locus. As a result, I find the title to be an overstatement of the findings of the paper and suggest the authors refocus on the more robust findings of the manuscript.
Live-cell imaging requires extensive engineering of the target loci. Perhaps this was lost in the Methods, but it is a 5-step process to integrate the stem-loops. We tried to engineer other loci, but this is far from trivial and this technique does not work for all loci tested. The hairpins are also unstable, and need to be carefully checked prior to experimentation, which challenges scaling this approach up to a higher-throughput. It appears that we undersold this point, but the fact that we now provide a locus and strains for the community that makes such studies possible for DNC represent a tremendous achievement. Since hda1D also decreases time between initiations, we generalized the finding to Hda1C.
However, we recognized that the reviewer makes a helpful suggestion to choose a more careful title since there is no statistically significant reduction of initiation frequency in some mutants. We have revised the title to “__Hda1C limits divergent non-coding transcription and restricts transcription initiation frequency__” in the revised manuscript to address this point.
#3.2. Relatedly, in Figure 4, the authors present the findings from the single molecule live cell imaging experiments. Within this experiment, the authors include a cac2 deletion (CAF-1 subunit) strain, and observe a modest effect, similar to hda1 deletion. This is surprising as the authors mentioned this location (GCG1/SUT098) was selected as CAF-1 was NOT shown to regulate the DNC previously (Marquardt et al 2014; as mentioned at the beginning of the Results section). The similar decrease in initiation frequency between cac2 deletion and hda1 deletion further concerns me regarding the use of these data as the headlining finding.
We believe there is a misunderstanding. We clarify that selection of the GCG1 locus was based on a cut-off value for cac2D effect, as is also shown in Fig S1C. The fold-change is small, but since DNC transcription of the chosen loci is high in wild type, an increase in a mutant would not necessarily give a high fold-change. Hence, we need to be cautious to conclude that CAF-I does not regulate DNC at this locus. The fold-change analysis suggested it, but it remained possible. CAF-I appears to affect even more loci than initially identified with the chosen cut-off. We see the same trend as in Hda1C mutants as in cac2, which offers support to the exciting idea that modulation of the initiation frequency may be a shared mechanism by chromatin-based regulators acting on DNC.
#3.3. It is unclear to me why the change in mRNA expression is included within the screen. Why not solely look at the expression change of the DNC? Importantly, the authors note in the discussion that perhaps the reason the SAGA complex was identified was due to regulating mRNA expression and not DNC expression and therefore was identified in the screen. Could the authors not just present the fold change in DNC expression using their YFP reporter, and not the YFP vs mCherry?
The regulation of initiation frequency in each direction is super-imposed on a general positive correlation __(rho = 0.26, p-value = 4.94e-24) between the coding and non-coding directions__, please see also RFig.1. For the purpose of this study about selective effects on the direction of transcription, it is vital to incorporate both sides of the reporter. Otherwise, we would select for factors that activate or repress the transcription from the target promoter NDR. This point is accessible in Fig.1D-E, where mutations that affect YFP usually also have an effect on mCherry. The aim of this study was to identify mutants that affect the relative expression, and therefore a focus on one fluorophore would not improve the analysis. We clarified this important point more accessibly in the revised manuscript (line 315).
Please also note that all the raw data are available, so colleagues are in the position to perform their independent analyses. We believe that it is very valuable for the community to have access to these data since they may be useful for other purposes and could be analyzed in many different ways. In fact, we have tried several methods and approaches over the years and present what we believe is most appropriate in this manuscript. For example, Hda1C comes out as a convincing hit with a range of different approaches to analyze the data, which is also a reason we feel confident about the characterization of Hda1C.
#3.4. This is absolutely beyond the scope of the paper, but limiting the screen to only nonessential proteins likely misses important regulators. In the future, perhaps the authors could pursue a SATAY screen to look for essential proteins as well? Again, the findings of this paper are appropriate, and the screen is a great undertaking, but I want to suggest this to the authors for potential future projects.
Thank you for this excellent suggestion. We agree that capturing the role of essential factors would be very informative, and the saturated transposition approach would be promising. However, as the reviewer points out, performing these analyses is beyond the scope of the current manuscript.
#3.5. The authors perform NETseq experiments in deletion strains and identify ~1500 DNC transcripts with altered expression. Later the authors look into the mechanism and demonstrate an increased H3ac in hda1 deletion strains. The authors could enhance the representation of these datasets by correlating the change in H3ac with the change in DNC transcription - do they correlate?
Thank you for bringing up this excellent point. We present the correlation data of change in H3ac and DNC transcription in the hda1D mutant (RFig5.). The ChIP-seq and NET-seq values of hda1D were divided by respective WT values in order to quantify the relative increase of H3 acetylation or nascent transcription in hda1D). The data showed a weak (Spearman rho= 0.23) but significant (pval=3.0e-20) positive correlation between the ratio values. The hda1D-dependent increase in H3 acetylation correlates with hda1D-dependent increase of RNAPII occupancy in DNC transcripts. We enhanced our representation of these data by including this plot as S5D in the revised manuscript as suggested.
(INSERT Rfig5)
RFig5__: Scatterplot of hda1D/WT NET-seq (y-axis) and ChIP-seq (x-axis) ratios. Each point corresponds to a bidirectional gene promoter overlapping with an NDR. The x-axis shows ChIP-seq ratios, and the y-axis shows the NET-seq ratios. These data support Spearman correlation test: rho = 0.234 and a statistically significant p-value = 3.0e-20.__
#3.6. In Figure 5, the authors argue that Hda1C works non-redundantly with K56ac, using point mutants to mutate K56 to A or Q. Did the screen identify anything else in the K56ac pathway? Rtt109 or Asf1, for example? Because Hda1C deacetylates H3, including but not limited to K56, it is a bit surprising the K56 point mutations result in a larger increase in SUT098-YFP levels. The authors discuss within the text that Hda1C has multiple targets; but coming back to my previous point that CAF-I was not supposed to impact this location, I am having a hard time understanding these results.
This is an excellent point. We improved the manuscript by highlighting other factors with links to H3K56ac in our scatter plots, for example Rtt109 in Fig 2A. Nevertheless, the reviewer may wish to satisfy his/her curiosity by exploring table S2 in more detail. Table S2 lists the top candidates from both screens.
We hope our answer to point #3.2 helped to clarify the aspect of this comment related to CAF-I.
**Minor comments**
#3.7. The authors follow up the screen using RTqPCR for GCG1/SUT098 in newly made deletion strains. I was surprised the authors choose this locus rather than the ORC2/SUT014 locus, as the screen showed a strong increase for this reporter. While I appreciate generating the deletion strains within the reporter is beyond necessary, assessing the endogenous locus within the deletion strains by RTqPCR seems reasonable.
We chose GCG1 locus since the fold change in directionality by genetic screen was high for the activator mutants. We will perform this experiment and add the missing validation experiment for the ORC2 locus in the revised manuscript.
#3.8. The authors tend to show their genomic data as metaplots; it would be nice to see heatmaps where more can be gleaned from the display of all the loci. This applies to the NET-seq data (Figure 3) and the ChIP-seq data (Figure 5).
We appreciate the suggestion and generated the requested heatmaps using the NET-seq tracks of WT and hda mutants (RFig6.). The heatmap represents the same genomic intervals as on the corresponding metagene plot (Figure 3A). We find that the differences between WT and hda samples are more clearly accessible at first glance on the metagene plot rather than on the heatmap. We believe that this could be because the heatmaps do not represent what transcripts have in common and rather underlines the differences. In contrast, the metagene plots reveal the common trends by taking the average of signal. We thus prefer showing metagene plots in the manuscript, as they allow for overlay of multiple tracks on the same plot, thus enhancing visual comparison for the readers.
(INSERT Rfig6)
RFig6. Heatmap representing NET-seq data in WT, hda1D and hda3D. Genomic intervals covering [TSS - 100 bp, TSS + 500 bp] of DNC transcripts (n=1517) are shown. The color indicates the log2-transformed NET-seq values.
#3.9. In Figure 5B, the authors present H3ac ChIP-seq data, presented as a ratio of H3ac/total H3. While this is a perfectly acceptable way to present the data, I was surprised to see a decrease in total H3 levels when examining the supplemental data. Has this decrease in H3 occupancy upon hda1 deletion been shown previously? This finding should be discussed within the manuscript.
We appreciate that the reviewer noticed this. We do not think this has been explicitly stated before, as the focus thus far had been on the effects towards the mRNA. However, the effect is not statistically significant between the WT and hda1D as observed in S5B. We thus prefer to remain cautious about this conclusion.
#3.10. In Supplemental Figure S3, the authors break down the NET-seq data by DNC FPKM, which is very nice. Very minor point that the font here is quite small.
Thanks, we improved the font size. Note that we also revised the y-axis scale in response to comment #1.4.
Reviewer #3 (Significance (Required)):
\*Significance:** *
The regulation of divergent non-coding RNAs is an understudied field. In this paper, the authors perform a screen for all non-essential yeast proteins in regulating the expression of these ncRNAs. The screen results and follow up defining the role of Hda1C in broadly repressing the expression of these ncRNAs is of interest to the field.
We are grateful to the reviewer for highlighting the interest of our work to the field.
\*Context:** *
This work follows from Marquardt's previous 2014 study that identify Caf1 as regulating DNCs in S. cerevisiae.
\*Audience:** *
Broadly, the chromatin and transcription field. Anyone interested in how chromatin regulates transcription, regulation of ncRNAs, and functions of histone modifying enzymes.
\*Expertise:** *
I am a member of the chromatin and transcription field, largely performing genomic experiments. We do not perform microscopy, although sufficiently understand the experiments and results presented here.
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Referee #3
Evidence, reproducibility and clarity
Summary:
In this manuscript, Gowthaman et al describe the results and follow up of their screen aimed at identifying regulators of divergent noncoding (DNC) transcription in S. cerevisiae. From this screen, they identify Hda1C as a repressor of DNC transcription, and perform follow experiments to support and detail this finding. In addition to RTqPCR to confirm the reporter and endogenous changes, the authors perform NET-seq to look at global DNC alteration upon Hda1C subunit deletion and identify a number of non-coding transcripts with altered expression levels. In addition, the authors perform live cell imaging to demonstrate that there is a modest restriction of initiation frequency when one of the subunits of Hda1C is deleted. Finally, the authors explore changes to pan-H3 acetylation and the genetic overlap between Hda1C and H3K56ac demonstrating independent genetic pathways, but overall increases in H3 acetylation over DNCs when Hda1C is deleted. Overall, the screen and results are of interest, but the authors overstate some of the conclusions (perhaps most importantly within the title!). I have the following suggestions to improve the manuscript:
Major comments:
- The title of the manuscript is based on the single molecule live cell imagining experiments presented in Figure 4. While there is a statistically significant decrease in initiation frequency from deletion of one Hda1C subunit, there is no statistical decrease in deletion of the other two. Furthermore, these experiments were performed at one locus. As a result, I find the title to be an overstatement of the findings of the paper and suggest the authors refocus on the more robust findings of the manuscript.
- Relatedly, in Figure 4, the authors present the findings from the single molecule live cell imaging experiments. Within this experiment, the authors include a cac2 deletion (CAF-1 subunit) strain, and observe a modest effect, similar to hda1 deletion. This is surprising as the authors mentioned this location (GCG1/SUT098) was selected as CAF-1 was NOT shown to regulate the DNC previously (Marquardt et al 2014; as mentioned at the beginning of the Results section). The similar decrease in initiation frequency between cac2 deletion and hda1 deletion further concerns me regarding the use of these data as the headlining finding.
- It is unclear to me why the change in mRNA expression is included within the screen. Why not solely look at the expression change of the DNC? Importantly, the authors note in the discussion that perhaps the reason the SAGA complex was identified was due to regulating mRNA expression and not DNC expression and therefore was identified in the screen. Could the authors not just present the fold change in DNC expression using their YFP reporter, and not the YFP vs mCherry?
- This is absolutely beyond the scope of the paper, but limiting the screen to only nonessential proteins likely misses important regulators. In the future, perhaps the authors could pursue a SATAY screen to look for essential proteins as well? Again, the findings of this paper are appropriate, and the screen is a great undertaking, but I want to suggest this to the authors for potential future projects.
- The authors perform NETseq experiments in deletion strains and identify ~1500 DNC transcripts with altered expression. Later the authors look into the mechanism and demonstrate an increased H3ac in hda1 deletion strains. The authors could enhance the representation of these datasets by correlating the change in H3ac with the change in DNC transcription - do they correlate?
- In Figure 5, the authors argue that Hda1C works non-redundantly with K56ac, using point mutants to mutate K56 to A or Q. Did the screen identify anything else in the K56ac pathway? Rtt109 or Asf1, for example? Because Hda1C deacetylates H3, including but not limited to K56, it is a bit surprising the K56 point mutations result in a larger increase in SUT098-YFP levels. The authors discuss within the text that Hda1C has multiple targets; but coming back to my previous point that CAF-I was not supposed to impact this location, I am having a hard time understanding these results.
Minor comments:
- The authors follow up the screen using RTqPCR for GCG1/SUT098 in newly made deletion strains. I was surprised the authors choose this locus rather than the ORC2/SUT014 locus, as the screen showed a strong increase for this reporter. While I appreciate generating the deletion strains within the reporter is beyond necessary, assessing the endogenous locus within the deletion strains by RTqPCR seems reasonable.
- The authors tend to show their genomic data as metaplots; it would be nice to see heatmaps where more can be gleaned from the display of all the loci. This applies to the NET-seq data (Figure 3) and the ChIP-seq data (Figure 5).
- In Figure 5B, the authors present H3ac ChIP-seq data, presented as a ratio of H3ac/total H3. While this is a perfectly acceptable way to present the data, I was surprised to see a decrease in total H3 levels when examining the supplemental data. Has this decrease in H3 occupancy upon hda1 deletion been shown previously? This finding should be discussed within the manuscript.
- In Supplemental Figure S3, the authors break down the NET-seq data by DNC FPKM, which is very nice. Very minor point that the font here is quite small.
Significance
Significance:
The regulation of divergent non-coding RNAs is an understudied field. In this paper, the authors perform a screen for all non-essential yeast proteins in regulating the expression of these ncRNAs. The screen results and follow up defining the role of Hda1C in broadly repressing the expression of these ncRNAs is of interest to the field.
Context:
This work follows from Marquardt's previous 2014 study that identify Caf1 as regulating DNCs in S. cerevisiae.
Audience:
Broadly, the chromatin and transcription field. Anyone interested in how chromatin regulates transcription, regulation of ncRNAs, and functions of histone modifying enzymes.
Expertise:
I am a member of the chromatin and transcription field, largely performing genomic experiments. We do not perform microscopy, although sufficiently understand the experiments and results presented here.
-
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Referee #2
Evidence, reproducibility and clarity
This reviewer considers himself a generalist with insight into chromatin-based gene regulation, but no first-hand experience with the yeast system or single-molecule imaging.
Promotors are frequently transcribed in both directions. The divergent, *upstream' transcript is frequently unstable. Transcription initiation is regulated through the acetylation of promoter-proximal nucleosomes, where HDAC-dependent deacetylation of histones typically represses transcription initiation. The current manuscript addresses the question whether initiation of coding and divergent, non-coding (DNC) transcription is regulated by the same factors. Previously Marquardt and others showed that H3K56ac-mediated histone exchange has a differential effect on coding and DNC transcription.
Using a clever reporter system, the authors screened for positive and negative regulators that preferentially affect DNC transcription. They discover the Hda1 deacetylase complex as a DNC-biased repressor and diverse HATs as DNC-biased activators. The role of activators could not be validated, presumably due to high variability of the system.
Focusing on Hda1c the authors present data suggesting a larger effect of Hda1c on 'upstream' nucleosomes associated with DNC transcription than in coding transcription. Genome-wide NET-seq mapping was consistent with this differential regulation. Life cell imaging of one specific case argues that Hda1-mediated repression reduced the time between initiation events. The authors employ state of the art methods and in general the data are of very good quality. The effect size is very small, which raises the broader question whether the results, while statistically significant is biological relevant. I have a few comments that the authors may use to revise their manuscript.
1) The differentially regulated coding and DNC transcription are defined by a directionality score. The screen was performed with two reporter loci that are strongly biased for DNC transcription (the idea to detect activators did not work out). Considering that coding and DNC transcription may not be totally independent because of the proximity of target nucleosomes, and sense and antisense transcription may compete for regulators, the question arises how levels of coding transcription affect DNC transcription in wildtype and mutants. The authors stratified their results according to levels of DNC transcription, but discussion and data analysis of the effect of coding transcription on the directionality score may be relevant.
2) The study is strong where the findings can be generalized. The single-molecule live-cell imaging analysis, while done properly, has only limiting impact, because the corresponding coding transcript could not be detected. This si more an anecdotal finding.
3) The effect size is small (20%, on average) and the variability is high. The fact that the HATs that emerged as very robust activators of DNC transcription could not be validated and that the Hda2 subunit of the HDAC complex was not found statistically significant show the limitations of the study. To their credit, the authors discuss these limitations appropriately.
4) Figure S3C suggests that the Hda effect is largest at genes that are poorly expressed, and smaller at more average expression levels. Are we looking at a phenomenon that mainly applies to repressed genes?
Minor issues
5) The NET-seq study involves two replicates. How well did they correlate?
6) For the live-cell imaging replicates were not mentioned. Were replicate studies performed?
7) Fig 4E is not mentioned in the text (mislabeled as 4D)
8) Fig S5 is not mentioned in the main text.
Significance
In summary, this is a high-quality study that presents the results of a genome-wide screen that will be of interest to colleagues in the narrower field. Due to the small effects the results may appeal less to a general readership.
-
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Referee #1
Evidence, reproducibility and clarity
In the paper by Gowthaman et al., the authors aim at better understanding the molecular mechanisms controlling divergent non-coding transcription (DNC). They describe a high-throughput yeast genetic screen using two strains in which two loci consisting of a coding and a divergent non-coding transcription unit (CGC1-SUT098 or ORC2-SUT014) were replaced by a bidirectional fluorescent reporter construct encoding mCherry in the coding direction and YFP in the non-coding direction. The two reporter strains were crossed with the yeast deletion library and mutants leading to increased or decreased YFP signal were selected as potential DNC repressors or activators. The two screens identified a number of common potential repressors and activators. Components of the Hda1C histone deacetylase complex were identified as DNC repressors in both screens. This phenomenon was confirmed genome-wide by performing NET-Seq in WT as well as hda1D and hda3D strains. This experiment allowed to identify 1517 DNC transcripts repressed by Hda1. Further analyses indicate that Hda1C represses DNC genome-wide independently of expression levels and that loss of Hda1 does not substantially affect coding transcription.
Live-cell imaging of transcription was then used to show that loss of Hda1 increases DNC transcription frequency rather than duration providing novel information on the link between DNC transcription initiation kinetics and chromatin regulation. Finally, using Chip-seq, the authors show that the level of acetylation over the divergent non-coding units is increased in the absence of Hda1 and some experiments suggest that H3K56 acetylation also contributes to DNC regulation, further strengthening the importance of elevated histone acetylation in efficient DNC.
Importantly, several components of the SWI/SNF chromatin remodeling complex were identified as activators confirming earlier observations (Marquardt et al., 2014). SAGA subunits were also among potential DNC activators, however these effects could not be confirmed through validation experiments. The authors conclude that DNC may be independent of specific activators and mainly due to transcriptional noise resulting from the adjacent NDR.
Overall this paper is very well structured, clearly written and the experiments are well controlled. The genetic screen identifies novel factors involved in the regulation of DNC. The study clearly demonstrates that the level of acetylation is a key regulator of divergent non-coding transcription and that histone deacetylation by Hda1 reduces the frequency of DNC initiation events. While this conclusion is strongly supported by the Net-Seq and Chip-seq metagene analyses, the fluorescence mCherry and YFP values or qRP-PCR analyses of specific genes do not always behave as expected when looking at absolute values rather than mCherry/YFP or GCG1/SUT098 ratios, which is sometimes disturbing when reading the paper. Therefore, the following points should be clarified.
Major points:
Figures 2 and S2A: Figures 2C and D show the mCherry/YFP fluorescence and GCG1/SUT098 RT-qPCR gene expression ratios respectively, which are consistent with a repressive effect of Hda1C on DNC transcription and a potential DNC activating effect of SAGA components. However, the absolute mCherry and YFP or GCG1 and SUT098 expression values presented in Figures S2A and S2B show the opposite: loss of Hda1C subunits rather leads to a decrease in mCherry with not much effect on YFP; moreover loss of Hda3 results in decreased SUT098, which is inconsistent with the whole model. The same comment is valid for the SAGA mutants. It would be good to provide some explanation for these a priori contradictory observations, especially for the Hda1c mutants, which are the major focus of the study. The Net-Seq analyses are certainly more reliable since less subject to protein or RNA stability effects, which may underlie some of the inconsistencies between protein and RNA absolute levels.
Figure 3: this figure examines the effect of Hda1 and Hda3 on the 1517 DNC transcripts. Does loss of this HDAC also increase the expression of all the other 2219 non-coding transcripts identified by Net-Seq, which would make Hda1C a more general repressor of non-coding transcription?
Moreover, does loss of Hda1 or Hda3 reveal DNC transcripts that were not detected in wild-type? This may increase even more the number of genes with divergent transcription.
Figures S3A, B, C: are the 3 groups of DNCs derepressed to the same extent by loss of Hda1 or Hda3? This is difficult to judge given the differences in y-axis scales. Figures S3D, E: the authors show the Net-Seq snapshots for the GCG1 and ORC2 loci. It would be good to add the quantifications as presented in Figure 3 for YPL172C and YDRr216C.
Figures S4A, B, C and D are not well explained. What does the y axis frequency correspond to? Is it the % of cells showing a signal? Is the intensity of SUT098 higher because the transcription initiation frequency is higher and therefore the transcription site signal is more intense?
Figures S4 A-I should be more specifically cited in the text.
Figure 5A: it is really unexpected and unclear why the mCherry/YFP in the WTH3/hda1D and WTH3/hda1D/H3K56mut is increasing compared to WTH3, since DNC is supposed to increase. Similar comment for Figure S5C. This should be clarified in the text.
More generally, as already mentioned above, the fluorescence data are expressed either as mCherry/YFP ratio or as absolute values. It would be good to systematically show the ratios and the absolute values of mCherry and YFP signal; the same for coding and DNC RT-qPCR as well as Net-Seq values when available.
Figures S5A and B are not referred to in the text. It should be mentioned and explained how normalization to H3 affects the levels of acetylated H3 over the NDR. p. 12 "Our data thus suggest to extend the transcriptional noise hypothesis with activities limiting DNC transcription to account for genome-wide variation in non-coding transcription".
If DNC is the result of "transcriptional noise", it is surprising that in the case of CGC1-SUT098, the transcription frequency is higher in the non-coding versus the coding direction. Is the SUT098 behaving like the coding unit in this case? The authors should comment on that.
Minor comments:
p. 4 should one talk about Hda1C-linked histone acetylation facilitates... (should be deacetylation...??) The authors should explain why they chose two coding/non-coding pairs that are cac2D insensitive and whether other criteria, such as level of DNC transcription, were also considered, since GCG1-SUT098 represents one of the most highly expressed divergent non-coding transcripts.
It is hard to understand why both the H3K56A and H3K56Q mutations lead to increased DNC, a result already presented in the Marquardt et al. 2014 paper. It would be helpful to provide a more extensive explanation or hypothesis.
What defines the level of DNC repression? How does the level of repression correlate with the level of coding transcription?
Significance
This is a very interesting and innovative study using cutting edge genetic approaches, genome-wide sequencing as well as single cell imaging to extend our understanding of non-coding transcription regulation and its potential impact on gene expression. It is a nice continuation and complement of an earlier study from the same author (Marquardt et al., 2014) and will certainly be of interest to a large chromatin biology audience.
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Reply to the reviewers
Point-by-point response:
*Reviewer #1 (Evidence, reproducibility and clarity (Required)):
**SUMMARY**
This MS tackles a largely unknown topic of vessel formation: how vessels anastomose and lumenise. The authors demonstrate that a matrix protein svep1 produced by neural tube during zebrafish embryogenesis plays a key role with blood flow to orchestrate anastomose formation. Actually in absence of this protein concomitantly with blood flow reduction results in significant decrease of lumenised DLAV segments.
In absence of svep1 they observed an expansion of apelin positive endothelial cells connected with a defect in tip/stalk cell specification. Interestingly the phenotype is amplified by blocking the kinase activity of VEGFR2
**MAJOR COMMENTS**
The most solid evidence on the role of blood flow in cooperating with svep1 relies on the use of tricaine, which reduces heart contractility. Interestingly the authors report some data by using embryo lacking cardiac troponin T2. In my opinion I suggest the author to better analyze the phenotype obtained by the deletion of svep1 together a dose-dependent reduction of tnnt2. This approach is more elegant and physiologic than the use of a chemical compound. Furthermore this approach will allow to better analyze the relations ship between blood flow and the expression of svep1 in neural tube. It should be relevant to establish a sort of flow threshold required to dampen lumenisation. *
Response: We appreciate the comment and have previously attempted to titrate the tnnt2 morpholino as published to have a graded reduction in blood flow. In our hands, this has not proved to be a robust approach, but we are willing to give it another try. In addition, we propose use alternative compounds to tricaine for blood flow reduction without affecting neural physiology. Alternatively we will use a-bungarotoxin mRNA injection to selectively affect neural activity to immobilize the embryos without effects on heart rate and blood flow (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC4526548/)
To further improve the findings here reported I suggest to analyze the expression of klf2, which is a well known mechano-sensor of blood flow in several animal species including zebrafish.
Response: We will perform klf2 expression analysis
It's likely that apelin is relevant in the observed phenotype. Which is the phenotype of a double mutant lacking both apl and svep1? Is there a direct influence of blood flow on apl expression?
Response: We will investigate the double loss of function. However, double mutants would take some time, and a combination of morpholino and mutant would likely be the first and best option to answer this question in a reasonable time frame. The effect of flow on apl expression can be tested.
Is there any suggestion that this mechanism is oprative in mammalian?
Response: This is an interesting question and certainly relevant for follow up studies. At present, we can only speculate on a possible connection with flow, given that Svep1 mutations have recently been associated with artherosclerosis. However, whether the anastomosis defect we identify is conserved remains to be seen.
*Reviewer #1 (Significance (Required)):
The data here reported might represent a step forward in the field because a new mechanism is suggested.
The interest is sufficiently broad.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
**Summary:**
The authors demonstrated that loss of svep1 in zebrafish contributed to defective anastomosis of intersegmental vessels, in addition, such Svep1 acted synergistically with blood flow to modulate vascular network formation in the zebrafish trunk.
**Major comments:**
The expression of svep1 is localized in neurons of neural tube, dorsal epithelial cells (as indicated by transgenic zebrafish) and ventral somite boundary (as indicated by in situ) but is excluded from endothelial cells nor the vasculature. It remains puzzling and the authors have not addressed this very reason of how a gene that is expressed in non-vascular tissue play a crucial role in vessel anastomosis, ie DLAV, ISV lumenization, during angiogenesis. As the entire story of this svep1 is related to its function in angiogenic sprout and lumen formation of vascular tissues, it will be helpful for reader to be able to put the pieces together of how such gene may be functionally involved in such angiogenic process. Previous publication of this gene involved in lymphoangiogenesis, as in this manuscript the authors could provide more evidence of how such gene and its localized expression contribute to different tissue in the vascular system, ie DLAV, instead of the neural tube, dorsal epidermis or ventral somite boundary.*
Response: We appreciate the wish to understand exactly how non-endothelial expression of Svep1 causes an endothelial phenotype selectively under reduced flow conditions. The very nature of this new phenotype requires analysis in vivo, and can not easily be transferred to an ex vivo assay. Therefore, selective loss of function in different cell populations is not easily available. More importantly, the interpretation of such efforts, when mosaic, are marred with issues. At this point, we feel that full molecular characterization of how Svep1 affects endothelial cells during anastomosis will require entirely new approaches and lies beyond what can be achieved in this manuscript.
We will however attempt to clarify the findings and the potential mechanisms in the discussion.
Another puzzling point is that tricaine is the center of the subject in this study. As the authors claim that tricaine-dependent blood flow reduction synergistically augmented the effect of svep1 deficiency. However, tricaine is known acting on neural voltage-gated sodium channels, whether svep1 function was affected by tricaine in the neural tissues and possibly its expression, the authors could provide more explanation and argument in the discussion.
Response: As mentioned in our response to reviewer 1, we will perform additional experiments to try to clarify whether an effect of tricaine on neuronal sodium channels contributes to the phenotype.
It is unclear on p12 "These results suggest that while svep1 loss-of-function produces a cardiac defect that enhances the effect of tricaine on reducing blood flow, svep1 has an additive effect in modulating blood vessels anastomosis" that svep1 deficiency enhances the effect of tricaine leading to reduced blood flow, however, it is not accurate to state that svep1 loss-of-function produces a cardiac defect. It is not sure if the effect of svep1 was actually neural rather than cardiovascular tissue, for example, tricaine acts on neural voltage-gated sodium channel that slowing down heart beat. Whether the authors can explore the possibility that svep1 function in neural rather than cardiovascular tissues, may be discuss why the authors think svep1 enhances the blood flow defect (tnnt2a knockdown or tricaine) on angiogenesis such as DLAV phenotype.
Response: We will attempt to dissect potential contributions by neural effects from cardiac and flow related effects as stated above. Tnnt2 MO and alternative drugs to reduce heart function selectively will be used. We will also clarify the discussion.
On p13, the authors stated that svep1 expression was inhibited by reduced blood flow, however, is it really the effect of reduced blood flow or caused by the chemical tricaine? If tnnt2a knockdown showed a similar phenotype, then it may be more convincing.
Response: see above
\*Minor comments:**
The work on "svep1 loss-of-function and knockdown are rescued by flt1 knockdown" was beautifully done and it is very clear and convincing.
The last two sections, "Vegfa/Vegfr signalling is necessary for ISV lumenisation maintenance and DLAV formation" and "Vegfa/Vegfr signalling inhibition exacerbates svep1 loss-of-function DLAV phenotype in reduced flow conditions" are more related to the flt1 knockdown phenotype. These 3 different sections are actually related in the sense that the rescue phenotype should be explained in the vegf signaling pathway. They are better off to discuss more cohesively about this vegf pathway that will help readers to appreciate more their work in svep1. *
Answer: We agree and will do so.
*Reviewer #2 (Significance (Required)):
This manuscript of svep1 in zebrafish provides new insight in angiogenesis, particularly in development of vessel anastomosis in zebrafish embryo, is very significant in the field and readers who are interested in angiogenesis and zebrafish development, including myself.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
This manuscript reports that the secreted extra-cellular matrix protein Svep1 plays a role in vascular anastomosis during developmental angiogenesis in zebrafish. Further, the study demonstrates that flow and Svep1 modulate the vascular network in a synergistic fashion. This is a high quality manuscript presenting novel data which compellingly support the conclusions that are made. I have no suggestions for further experimentation but list minor points below.
- The final paragraph of Discussion is underdeveloped in that it claims regulation of phenotypic robustness in angiogenesis and its failure promises crucial insights into the mechanisms causing breakdown of vascular homeostasis in human disease. However, this issue is not pursued in any substantial way in Discussion. For example, are there known mutations in humans which lead to anastomosis defects and, if so, do any of them relate to the molecules or signaling pathways which are the subject of this manuscript? *
Response: We agree with the wish to see more substantial discussion of the issue of phenotypic robustness and potential links to human disease. The question of anastomosis itself is something that has not been addressed in humans, as it is a rather detailed phenotype observable where predictive patterning occurs and can be dynamically studied. As such, there is a lack of literature and knowledge on signalling pathways that drive anastomosis in humans, and also not many that have been identified in experimental systems or animal models. Flt1 and Vegf signalling, junctional molecules and a few other pathways have been shown to be involved, but nothing is known so far about Svep1 and anastomosis in other system. We will attempt to complement the discussion to make this more clear.
- There are typographical errors in the text so a further proof-read is required. *
Response: thank you, these will be corrected
*Reviewer #3 (Significance (Required)):
This manuscript provides an incremental conceptual advance in our understanding of the molecular mechanisms responsible for vascular anastomosis during developmental angiogenesis. The manuscript will be of interest to developmental biologists and vascular biologists.
My field of expertise pertains to angiogenesis and lymphangiogenesis in the setting of cancer and other diseases. *I am not a developmental biologist.
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Referee #3
Evidence, reproducibility and clarity
This manuscript reports that the secreted extra-cellular matrix protein Svep1 plays a role in vascular anastomosis during developmental angiogenesis in zebrafish. Further, the study demonstrates that flow and Svep1 modulate the vascular network in a synergistic fashion. This is a high quality manuscript presenting novel data which compellingly support the conclusions that are made. I have no suggestions for further experimentation but list minor points below.
- The final paragraph of Discussion is underdeveloped in that it claims regulation of phenotypic robustness in angiogenesis and its failure promises crucial insights into the mechanisms causing breakdown of vascular homeostasis in human disease. However, this issue is not pursued in any substantial way in Discussion. For example, are there known mutations in humans which lead to anastomosis defects and, if so, do any of them relate to the molecules or signaling pathways which are the subject of this manuscript?
- There are typographical errors in the text so a further proof-read is required.
Significance
This manuscript provides an incremental conceptual advance in our understanding of the molecular mechanisms responsible for vascular anastomosis during developmental angiogenesis. The manuscript will be of interest to developmental biologists and vascular biologists.
My field of expertise pertains to angiogenesis and lymphangiogenesis in the setting of cancer and other diseases. I am not a developmental biologist.
-
Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.
Learn more at Review Commons
Referee #2
Evidence, reproducibility and clarity
Summary:
The authors demonstrated that loss of svep1 in zebrafish contributed to defective anastomosis of intersegmental vessels, in addition, such Svep1 acted synergistically with blood flow to modulate vascular network formation in the zebrafish trunk.
Major comments:
The expression of svep1 is localized in neurons of neural tube, dorsal epithelial cells (as indicated by transgenic zebrafish) and ventral somite boundary (as indicated by in situ) but is excluded from endothelial cells nor the vasculature. It remains puzzling and the authors have not addressed this very reason of how a gene that is expressed in non-vascular tissue play a crucial role in vessel anastomosis, ie DLAV, ISV lumenization, during angiogenesis. As the entire story of this svep1 is related to its function in angiogenic sprout and lumen formation of vascular tissues, it will be helpful for reader to be able to put the pieces together of how such gene may be functionally involved in such angiogenic process. Previous publication of this gene involved in lymphoangiogenesis, as in this manuscript the authors could provide more evidence of how such gene and its localized expression contribute to different tissue in the vascular system, ie DLAV, instead of the neural tube, dorsal epidermis or ventral somite boundary.
Another puzzling point is that tricaine is the center of the subject in this study. As the authors claim that tricaine-dependent blood flow reduction synergistically augmented the effect of svep1 deficiency. However, tricaine is known acting on neural voltage-gated sodium channels, whether svep1 function was affected by tricaine in the neural tissues and possibly its expression, the authors could provide more explanation and argument in the discussion.
It is unclear on p12 "These results suggest that while svep1 loss-of-function produces a cardiac defect that enhances the effect of tricaine on reducing blood flow, svep1 has an additive effect in modulating blood vessels anastomosis" that svep1 deficiency enhances the effect of tricaine leading to reduced blood flow, however, it is not accurate to state that svep1 loss-of-function produces a cardiac defect. It is not sure if the effect of svep1 was actually neural rather than cardiovascular tissue, for example, tricaine acts on neural voltage-gated sodium channel that slowing down heart beat. Whether the authors can explore the possibility that svep1 function in neural rather than cardiovascular tissues, may be discuss why the authors think svep1 enhances the blood flow defect (tnnt2a knockdown or tricaine) on angiogenesis such as DLAV phenotype.
On p13, the authors stated that svep1 expression was inhibited by reduced blood flow, however, is it really the effect of reduced blood flow or caused by the chemical tricaine? If tnnt2a knockdown showed a similar phenotype, then it may be more convincing.
Minor comments:
The work on "svep1 loss-of-function and knockdown are rescued by flt1 knockdown" was beautifully done and it is very clear and convincing.
The last two sections, "Vegfa/Vegfr signalling is necessary for ISV lumenisation maintenance and DLAV formation" and "Vegfa/Vegfr signalling inhibition exacerbates svep1 loss-of-function DLAV phenotype in reduced flow conditions" are more related to the flt1 knockdown phenotype. These 3 different sections are actually related in the sense that the rescue phenotype should be explained in the vegf signaling pathway. They are better off to discuss more cohesively about this vegf pathway that will help readers to appreciate more their work in svep1.
Significance
This manuscript of svep1 in zebrafish provides new insight in angiogenesis, particularly in development of vessel anastomosis in zebrafish embryo, is very significant in the field and readers who are interested in angiogenesis and zebrafish development, including myself.
-
Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.
Learn more at Review Commons
Referee #1
Evidence, reproducibility and clarity
SUMMARY
This MS tackles a largely unknown topic of vessel formation: how vessels anastomose and lumenise. The authors demonstrate that a matrix protein svep1 produced by neural tube during zebrafish embryogenesis plays a key role with blood flow to orchestrate anastomose formation. Actually in absence of this protein concomitantly with blood flow reduction results in significant decrease of lumenised DLAV segments.
In absence of svep1 they observed an expansion of apelin positive endothelial cells connected with a defect in tip/stalk cell specification. Interestingly the phenotype is amplified by blocking the kinase activity of VEGFR2
MAJOR COMMENTS
The most solid evidence on the role of blood flow in cooperating with svep1 relies on the use of tricaine, which reduces heart contractility. Interestingly the authors report some data by using embryo lacking cardiac troponin T2. In my opinion I suggest the author to better analyze the phenotype obtained by the deletion of svep1 together a dose-dependent reduction of tnnt2. This approach is more elegant and physiologic than the use of a chemical compound. Furthermore this approach will allow to better analyze the relations ship between blood flow and the expression of svep1 in neural tube. It should be relevant to establish a sort of flow threshold required to dampen lumenisation.
To further improve the findings here reported I suggest to analyze the expression of klf2, which is a well known mechano-sensor of blood flow in several animal species including zebrafish.
It's likely that apelin is relevant in the observed phenotype. Which is the phenotype of a double mutant lacking both apl and svep1? Is there a direct influence of blood flow on apl expression?
Is there any suggestion that this mechanism is oprative in mammalian?
Significance
The data here reported might represent a step forward in the field because a new mechanism is suggested.
The interest is sufficiently broad.
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- May 2021
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Reply to the reviewers
We thank the reviewers for their comments, criticisms and suggestions that will help to improve the quality of our manusrcipt.
Please find enclosed in this initial response our answer to each point raised by the reviewers.
Please note that for several answers normally come along with an additional figure that could be added in the full revised version of the manuscript. However, these additional figures could not be added in the way we have to submit our answers but we are ready to send a pdf file including our answers with the additional figures upon request.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
The paper by Genest et al. describes the effect of flotillins and sphingosine kinase 2 to stabilize AXL as a mechanism to promote epithelial-mesenchymal transition in breast (cancer) cells. The potential role of vesicles trafficking EMT-promoting proteins is of high interest in the field, also for exploring new opportunities of pharmacological targeting. However, the paper fails to convincingly demonstrate that the proposed mechanism is of real importance to support or promote EMT for the following main reasons:
1-a) The role of flotillins is studied only by overexpression and in the context of non-cancerous MCF10A cells, while breast cancer cells of epithelial-like origin are not analyzed.
Regarding the first part of the point raised here, we are not sure to understand correctly the sentence “[…] while breast cancer cells of epithelial-like origin are not analyzed”. Indeed, we used the breast cancer cell line MDA-MB-231 and a derived cell line that we generated by knocking down flotillin expression (MDA-MB-231shFlot2) in the second part of this study (Figure 6C, F and H and S7A, E and F). This previously characterized cell line allowed us to demonstrate that abolishing flotillin overexpression was sufficient to significantly inhibit the invasive properties of MDA-MB-231 cells (Planchon et al, J Cell Science 2018, https://doi.org/10.1242/jcs.218925
Although flotillin upregulation induces some major mechanisms of the EMT process in MCF10A cells, flotillin downregulation was not sufficient to reverse the EMT phenotype in MDA-MB-231 cells. This could be explained by the fact that EMT is a multifactorial process and that MDA-MB-231 cells went through too many irreversible changes leading to this process. By contrast, when we analyzed EMT markers after SphK2 inhibition or knock down in MCF10AF1F2 and in MDA-MB-231 cells (Figure 6A-C), we could observe a significant decrease in ZEB1 expression.
1-b) This is contrast with the purpose of the paper (see abstract, introduction, patients' data) which is to study tumors and EMT. Effect of shRNAs is also not reported, making it difficult to estimate the importance on the EMT phenotype.
As we mentioned in our manuscript, previous studies by other groups who downregulated flotillin expression in different cancer cell lines using siRNA approaches or re-expression of miRNAs that inhibit flotillin expression, already showed flotillin participation in EMT (for review please see, Gauthier-Rouvière et al, Cancer Metastasis Review, 2020, **doi: 10.1007/s10555-020-09873-y).
In this context, the novelty and the first goal of our study was to investigate how strong is the contribution of flotillin upregulation to EMT induction. To achieve this goal, we chose on purpose to use non-tumoral epithelial cells that do not harbor the anomalies already favoring EMT, unlike the cancer cell lines used in previous studies. In these non-tumoral models (the human MCF10A and mouse NMuMG mammary epithelial cell lines), we ectopically overexpressed flotillins (MCF10AF1F2 and NMuMGF1F2) to levels similar to what observed in invasive breast cancer cells. Using this approach, we found that flotillin overexpression is enough to induce EMT.
1-c) Then, alteration of EMT should be concluded also from other non-genetic functional parameters, not just by markers. For instance: was morphology of the cells changed? Was cell migration affected with F1F2?
Our conclusion that flotillin upregulation is sufficient to induce EMT in MCF10AF1F2 and NMuMGF1F2 cells is not based only on genetic functional parameters or markers. For instance, Figure S1 (panels H and I) shows a strong modification of the cell morphology and of the actin cytoskeleton organization in NMuMG cells upon flotillin upregulation. NMuMGF1F2 cells became flat and lost their apical F-actin belt and exhibited an increase in stress fibers.
As shown below (Additional Figure 1), similar modifications of the cell morphology and of the F-actin cytoskeleton organization occur also when flotillins are upregulated in MCF10A cells (see below the comparison of MCF10A and MCF10AF1F2 cells) (these data could be added in the manuscript).
ADDITIONAL FIGURE 1 CAN NOT BE ADDED BUT IS AVAILABLE UPON REQUEST
Additional figure 1: Upregulation of flotillins in MCF10A cells leads to changes in the cell morphology and in F-actin cytoskeleton organization. Comparison of the morphology and of the actin cytoskeleton organization in MCF10AmCh and MCF10AF1F2 cells. Confluent cells were fixed and stained for F-actin (green) using Alexa488-conjugated-Phalloidin and for nuclei (blue) using Hoechst (in panel A flotillin2-mCherry signal is shown). (A) Upper panels show the maximum intensity projection images (MIP) of MCF10AmCh (control) and MCF10AF1F2 (flotillin overexpression) cells obtained from a stack of images acquired by confocal microscopy. Lower panels show magnified images from the boxed areas, including one single plane and the x-z and y-z projections along the indicated axes. (B) 3D reconstruction images obtained from the region in the boxed area from the MIP-images shown in A.
These data show that in MCF10AF1F2 cells the apical actin belt is lost and the height of the cellular monolayer is lower compared with control MCF10AmCh cells.
We also analyzed the migration capacity of these cells (shown in Figure 3G of the submitted manuscript). Briefly, using a Boyden chamber assay, we showed that flotillin upregulation significantly increased migration of MCF10A cells (Figure 3G). We previously demonstrated that flotillin upregulation also promotes cell invasion in 3D using a spheroid assay (Planchon et al, J Cell Science, 2018, https://doi.org/10.1242/jcs.218925**). As shown below (Additional Figure 2), using a wound healing assay, we also observed that cell velocity is higher in flotillin-overexpressing NMuMGF1F2 cells than in control NMuMG cells (this could be added to the manuscript).
ADDITIONAL FIGURE 2 CAN NOT BE ADDED BUT IS AVAILABLE UPON REQUEST
Additional figure 2: Upregulation of flotillins in NMuMG cells increases cell velocity in a 2D migration assay. (A) Representative images of NMuMGmCh (control) and NMuMGF1F2 cells during wound healing. The yellow dashed line indicates the leading edge of the migrating monolayer at the indicated times. The trajectory of 60 individual cells was tracked and the cell velocity and persistence of migration were extracted. The histogram shows the velocity quantification (mean ± SEM of 4 independent experiments). (B) Representative trajectories of individual cells.
2) AXL up-regulation is not very strong (2-fold). What is unclear is if the minimal AXL increase due to F1F2 really provides a significant contribution to the EMT phenotype (as the authors conclude). The siRNA experiment knocks down all AXL, not just the F1F2-induced levels, making it difficult to estimate the real effect of the mechanism proposed.
As shown in figure 3A and D, in MCF10AF1F2 cells compared with MCF10AmCh cells, we measured a significant 2.5 ± 0.7-fold increase in the AXL protein level. We do not think that this can be considered as a minimal increase.
Considering that flotillin upregulation may affect simultaneously different receptors (Figure S2I, Figure S6A-F), we did not expect that downregulating a single receptor would have a major impact on the level of EMT markers and on cell migration. Yet, after knocking down AXL in MCF10AF1F2 cells, we observed a decrease in ZEB1 and N-cadherin expression and the re-expression of E-cadherin (Figure 3D-F) and the inhibition of cell migration (Figure 3G). The fact that we observed such an effect by downregulating AXL, which according to Reviewer #1 is minimally increased, might be explained by its well-known ability to act not alone but through cross-talk with other signaling receptors (Graham et al, Nature Reviews Cancer 2014; Halmos and Haura, Science Signaling 2016; Colavito et al, Journal of Oncology 2020).
As suggested by Reviewer #1, ideally, it would be interesting to bring back AXL to its level in MCF10AmCh cells to better evaluate only the contribution of its increase. However, adjusting so precisely the efficacy of AXL downregulation by siRNA seems quite difficult to achieve.
3) Why didn’t the author focus on EphA4 (or to a lesser extent ALK), which showed better regulation ?
As we mentioned (page 18) “the available tools allowed us to validate this result only for AXL, but not for EphA4 and ALK”**.
Nevertheless, for EphA4, we showed in Figure S6 that it is located in flotillin-positive late endosomes (Figure S6 A and C, for MCF10AF1F2 and NMuMGF1F2 cells, respectively) in a phosphorylated form (using an antibody against P-Y588/Y596-EphA4 that works in NMuMG cells, Figure S6D). However, the signals obtained by western blotting using the same antibody were too low to validate any significant variation of EphA4 Y-phosphorylation status, as suggested by the results from the phospho-RTK array.
Regarding ALK, the increase in its phosphorylation, suggested by the phospho-RTK array, remains puzzling to us. By western blotting of cell lysates and in the presence of positive controls, we did not detect any positive signal for phosphorylated ALK and even for total ALK in MCF10A and MCF10AF1F2 cells. In addition, to our knowledge, ALK expression in MCF10A cells has never been reported in the literature. These observations did not encourage us to pursue our investigations on ALK.
Moreover, several points led us to focus on AXL. Indeed, AXL expression is associated with the acquisition of a mesenchymal cell phenotype, invasive properties, and resistance to treatments and AXL is an attractive therapeutic target against which several inhibitors are in preclinical and clinical development (Shen Y et al. Life Sciences 2018). Moreover, AXL expression in tumors is attributed to post-transcriptional regulation, but the mechanisms are totally unknown. Understanding how its stabilization and signaling can be triggered by flotillin-mediated endocytic pathways is new and of high significance for the cancer field and the trafficking community.
3) The conclusions of the manuscript are contradicted by the reported clinical data. In Figure S4 the authors clearly observe co-expression of Flotillin 1 and AXL prevalently in luminal breast cancers, which is the subtype known to not be driven by EMT. This evidence already indicates that this (otherwise interesting) mechanism is not relevant to EMT in breast cancer. So, the conclusions are not supported by the data, and the experimental setup and model chosen are not appropriate to generalize the findings to cancer.
We acknowledge that flotillin 1/AXL co-expression is highest in the luminal subtype. If this co-expression was observed only in this particular subtype, we would have agreed that it excluded that flotillins and AXL co-overexpression may participate in EMT in tumor cells. However, our results show that flotillin 1 and AXL are co-expressed also in other subtypes that have undergone EMT. Considering this observation and the influence of flotillin upregulation on AXL overexpression we reported here, we believe that the point raised by the Reviewer is not sufficient to exclude that the co-upregulation of flotillins and AXL can participate in EMT induction in breast cancer cells.
**Minor (here the most important):**
4) The point of the Figure 2 is not clear. Why this part should have such a central role in the story? The entire data presented are not followed up in the rest of the paper. Moreover, in some cases upregulations also questionably significant (like RAS and STAT3 are not even 2 fold).
Moreover, the error bars are so small that it seems unrealistic that the plots indicate three independent experiments.
Because the activation of oncogenic signaling pathways is crucial to promote EMT, we think that analyzing these pathways in the context of flotillin upregulation is coherent with the message of the paper.
To our knowledge, the amplitude of up- or down-regulation has nothing to do with its significance. The amplitude also depends strongly on the context (stimulation with an agonist, overexpression of GEF, etc). For instance, increases lower than 2-fold are frequently reported (Bodin and Welch, Mol Biol Cell, 2005; Miura SI et al, Arteriosclerosis, Thromb and Vasc Biology, 2003; Matsunaga-Udagawa R et al, J Bio Chem 2010)** when assessing the activity of Ras or small GTPases, but they represent real upregulations. Furthermore, Ras activation is supported by the downstream 4-fold activation of ERK that we measured (Figure 2C).
In Figure 2, panels B, C, E, F and J, considering the amplitude of the mean increases shown, the error bars corresponding to SEM do not seem disproportionately small.
As the Reviewer seems to insinuate that we have not performed independent experiments, we are presenting in the table below the detailed results all obtained from independent experiments.
Panel
Parameter measured
Number of independent experiments
Fold of increase value in MCF10AF1F2 cells compared with MCF10AmCh cells in each experiment
Mean
SEM
p-value
B
Ras-GTP
5
1.95 ; 1.96 ; 1.18 ; 1.67 ; 1.86
1.72
0.14
0.001
C
Phospho- ERK
5
1.24 ; 5.43 ; 3.22 ; 6.11 ; 3.52
3.71
0.73
0.0042
E
Phospho-AKT
4
2.29 ; 6.54 ; 3.76 ; 2.6
3.8
0.97
0.0276
F
Phospho-STAT3
4
1.63 ; 1.63 ; 2.42 ; 1.60
1.82
0.20
0.0066
J
Phospho-SMAD3
8
4.1 ; 5.12 ; 6.29 ; 1.82 ; 2.58 ; 6.66 ; 2.82 ; 5.40
4.35
0.64
0.0001
In the legend to figure 2 panels C, E, F, J, “The histograms show […] with control MCF10AmCh **cells calculated from 4 independent experiments” was corrected by “The histograms show […] with control MCF10AmCh cells calculated from at least 4 independent experiments” as data shown in panel J were actually calculated from 8 independent experiments.
5) More robust statistical analysis should be provided in the Figure 1 to support that EMT is suppressed with F1F2 overexpression. For instance a more standard GSEA on hallmark signatures.
To avoid confusion, we understand that Reviewer #1 meant “… that EMT is induced with F1F2 overexpression” and not “… suppressed …”.
As recommended by Reviewer #1, we performed a GSEA on the hallmark signature and the results are already included in the current revised version of our manuscript (figure 1C).
6) In Figure 3 E-Cadherin is rescued with siAXL in the IF but not in the western blot.
Using siRNA transfection, we can have a mosaic effect due to the fact that not all the cells of the sample are transfected and thus efficiently knocked down. This mosaicism was clear when we analyzed E-cadherin by immunocytochemistry. Indeed, in some cells, probably the ones that have been more efficiently transfected with the AXL siRNA, E-cadherin expression is clearly seen. By western blotting, which provides a global analysis in which transfected and non-transfected cells are mixed, this was not significantly higher than in MCF10AF1F2 cells transfected with a control siRNA, although there was a trend towards increased E-cadherin expression in MCF10AF1F2 transfected with the AXL siRNA.
For the revised version of our manuscript we will try to improve the efficacy of the AXL siRNA and test whether we can fully rescue E-cadherin expression. The corresponding panel could be modified according to the data we will obtain.
7) Some sentences require clarifications. The authors should be more clear on why ZEB2 antibody was not available or what they mean with "Unfortunately the available tools..".
Page 7: we wrote «no anti-Zeb2 antibody is available». We should have said: «none of the anti-Zeb2 antibodies tested worked in MCF10A cells». We decided to remove “no anti-Zeb2 antibody is available” from the sentence to avoid confusion in the revised version of our manuscript.
Page 19: we wrote «unfortunately the available tools» to refer **the available tools against EphA4 and ALK that did not allow us to validate the data obtained using the phospho-RTK array showing that the Y-phosphorylation of these two RTK is increased in cells with upregulated flotillins. (see also our answer to major point 2).
8) Western blot from the CHX experiment should be shown, at least in the supplements. Again, the standard deviation in this experiment is minimal, was this really an average of three independent experiments (and not three western on the same lysates)?
As asked, a representative western blot is now shown in Figure 3C in the current revised version of the manuscript.
As indicated in the legend to the figure already in the initial version of our manuscript: “**The results are the mean ± SEM of 6 to 8 independent experiments depending on the time point, and are expressed as the percentage of AXL level at T0”. We wish to reassure Reviewer#1 that the results are really based on western blots performed on different lysates obtained in independent experiments. We can show the Reviewer these data obtained from independent experiments if necessary.
9) All conclusions are derived from one single cells MCF10a. NMuMG cells are shown at the beginning but not used for the rest of the paper. Anyway, if this wants to be a cancer research paper, then cancer cells needs to be used.
It is true that we did not use a cancer cell line at the beginning of the paper because, as expected, flotillin knock-down did not allow to revert the mesenchymal phenotype of MDA-MB-231 cells toward an epithelial one. If this had been obtained, we would have used these cells from the beginning of the paper. The lack of reversion of the mesenchymal phenotype after flotillin knock-down was expected. Indeed, the EMT process is multifactorial and the decrease of flotillins alone is obviously not sufficient to reverse it in a tumor cell line bearing multiple oncogenic mutations. Moreover, because we wanted to assess whether flotillin upregulation is sufficient in normal cells to acquire the properties of tumor cells and particularly to induce EMT, we used human MCF10A and murine NMuMG cells, two non-tumoral epithelial cell lines. Until now, the studies carried out on the effects of flotillin overexpression have used tumor cells that already harbor pro-oncogenic perturbations, preventing to show that flotillin overexpression alone activates oncogenic processes leading to EMT, and to identify the downstream mechanisms.
Nevertheless, we have used the MDA-MB-231 cell line in several experiments to analyze: i) AXL distribution and internalization following the knock-down of flotillins (Figures 4 and S5), ii) SphK2 and flotillin 2 co-localization and co-endocytosis (Figures 5A and D and S7A), iii) the impact of SphK2 inhibition on AXL expression level distribution and endocytosis (Figure 6), iv) SphK2 expression level upon flotillin knock-down (Figure S7E) and AXL expression level upon SphK1 inhibition (Figure S7F). With these experiments performed in MDA-MB-231 cells, we showed that AXL and SphK2 colocalize in flotillin-positive late endosomes and are co-endocytosed from the plasma membrane containing flotillin-rich domains to flotillin-positive vesicles. We also demonstrated that flotillins and SphK2 control the rate of AXL endocytosis and its stabilization.
We recently obtained additional data with HS578T cells, another triple negative breast cancer cell line, on the co-trafficking of AXL and flotillins as well as the co-trafficking of SphK2 and flotillins (Additional Figure 3, this data could be added in the fully revised version of our manuscript).
In addition, we observed that inhibiting SphK2 also decreased the level of AXL in HS578T cells. This data could be added in the revised version of the manuscript (see data in our answer to Point #1 from Reviewer #3).
- ADDITIONAL FIGURE 3 CAN NOT BE ADDED BUT IS AVAILABLE UPON REQUEST*
Additional figure 3: Co-trafficking of SphK2 and AXL with flotillin 1 in intracellular vesicles in HS578T cells. HS578T cells co-expressing Flot1-mCherry with SphK2-GFP (A) or AXL-GFP (B) were monitored by time lapse spinning disk confocal video-microscopy. On the right of each panel are shown still images at different time points (min) of the boxed area. The colored arrows allow following three distinct vesicles that are positive for Flot1-mCherry and Sphk2-GFP, or AXL-GFP.
10) The methods section contains inconsistent data about patients' samples (9 are indicated, but the Figure S4 features 37). Then, where those other 527 come from?
We corrected the manuscript and added all characteristics regarding the 37 patients in the “Supplementary information” section.
The 527 patients are from another cohort and were used for the analysis of the correlation between the mRNA levels of FLOT1 and p63 in breast cancer biopsies from 527 patients (Figure 2I). This cohort was described in our previous study (Planchon et al. J Cell Science 2018, https://doi.org/10.1242/jcs.218925). In the revised version of our manuscript, we now refer to this previous article in the “Result” section and in the legend to figure 2I to explain the origin and characteristics of this cohort.
11) Some figures do not match with the legends or with the description in the text. It has not been easy to review this paper.
We apologize as we indeed made one mistake in figure 2 that was inserted into the manuscript and that was actually figure S2 (that appeared twice). However, the correct figure 2 was uploaded on the website of Review Commons and BioRxiv. Regarding the comments made in point 4, it seems that Reviewer #1 examined the correct figure 2 that was uploaded and that matches the legend indicated in the manuscript.
Besides this mistake, we do not see any other mismatch between figures and legends.
Reviewer #1 (Significance (Required)):
I am a cancer biologist working on EMT.
**Referee Cross-commenting** I have nothing to comment on other's reviews.
Reviewer #2 (Evidence, reproducibility and clarity (Required)): Genest and co-authors present in this paper new fascinating evidence on how intracellular trafficking can modulate oncogenic signalling.
First of all, they show how overexpression of Flotillin1 and 2 in non-cancerous breast lines can induce a strong reprogramming towards an EMT phenotype. They analyse mRNA and protein expression, intracellular distribution of activated proteins, cell phenotypes to demonstrate a strong activation of oncogenic signalling pathways. They then identify AXL as a key player in this process and show how this protein is stabilised upon Flotillin expression. The authors use an amazing variety of approaches to study the endocytosis and the trafficking of endogenous, GFP-tagged, Halo-tagged and Myc-tagged AXL in different cell lines and their data are strong and very convincing, the images are of very high quality and the analysis rigorous. Their data strongly support the hypothesis that high Flotillin levels triggers AXL endocytosis and accumulation in non-degradative late endosomes where signalling remains active. The authors then show how SphK2 has a key role in AXL stabilisation, it colocalises with Flotillin, AXL and CD63 and its activity (which they block by using inhibitors or siRNA) is necessary for flotillin-induced AXL stabilisation and EMT induction. The paper is extremely well written, the data flow logically and they are appropriately presented and analysed. I don't have any major comment and I believe the paper is suitable for publication.
We thank the Reviewer for the positive appreciation on our manuscript.
I have only some minor comments/questions: 1) did the authors try to colocalise AXL with endogenous Flotillin in MDA-MB-231 cells? They could use the antibodies used in Fig S1B. Of note, the authors have shown it in luminal tumours in Fig S4C.
We performed co-immunofuorescence experiments to detect endogenous AXL with endogenous Flotillin in MDA-MB-231 cells. As shown below (Additional Figure 4), we could find AXL and Flotillin being present in the same intracellular endosomes. Images could be added in the revised version of the manuscript.
ADDITIONAL FIGURE 4 CAN NOT BE ADDED BUT IS AVAILABLE UPON REQUEST
Additional figure 4: Endogenous AXL and flotillin 1 are found in the same in intracellular vesicles in MDA-MB-231 cells. MDA-MB-231 cells were fixed and labelled with relevant antibodies directed against Flotillin1 and AXL. Scale bar in the main image : 10 µm. Scale bars in the magnified images from the boxed area : 1 µm. Arrows indicate flotillin and AXL positives vesicles
2) In Fig6G, it appears that AXL-Flotillin colocalization is lost upon SphK2 inhibition. Is this the case? It could be that the correct lipids are necessary for the formation of Flotillin-positive internalisation domains and this could be very interesting and reinforce the model proposed in the paper.
In figure 6G, cells were not permeabilized. Thus, only AXL at the cell surface was labelled using an antibody against the extracellular domain of AXL. Because flotillin 2 is tagged with mCherry, this allowed its visualization revealing its localization both at the cell surface and intracellularly in the inset of the lower pane l of figure 6G.
After 6 hours of treatment using the opaganib inhibitor, we did not notice any major change in AXL-flotillin colocalization at the cell surface. Somehow, this is expected because blocking the generation of S1P is more likely to inhibit the invagination of flotillin-rich membrane microdomains rather than their formation.
3) I would remove the sentence on line 995-997 "to our knowledge this is the first report to describe ligand-independent AXL stabilization..." as the cells are not serum starved in all experiments and animal serum can contain variable amounts of the ligand GAS6.
We understand and agree with Reviewer #2, this sentence has been modified by “**To our knowledge this is the first report to describe AXL stabilization following its endocytosis”
Please note that the authors don't have to necessarily address comments 1-2, their paper is already very rich in convincing data.
Reviewer #2 (Significance (Required)):
AXL is a major oncogene that promotes EMT in a variety of tumour types. Understanding how its signalling can be triggered by endocytic pathways even in cells that are non-cancerous is very important and of high significance for the cancer field and the trafficking community.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
This is an interesting and well written paper describing that upregulated flotillin promotes an endocytic pathway called upregulated flotillins-induced trafficking (UFIT) that mediates AXL endocytosis and allows its stabilization. Consequently, stabilized AXL in these flotillin-positive late endosomes enhances activation of oncogenic signaling pathways that promotes EMT. The authors suggest that Flotillin upregulation-induced AXL stabilization requires the activity of SphK2. However, this latter point is not supported by the data and further studies are needed to support this important conclusion.
**Major concerns:**
Most of the conclusions are based on effects of high concentrations (50 uM) of an ill-defined SphK2 inhibitor. The experiment described in Figure 6C-H need to be confirmed by downregulation of SphK2.
We understand that Reviewer #3 is concerned that in our experimental conditions, the effects we observed could be really explained by a specific inhibition of SphK2.
From the literature, among all the inhibitors described for SphK2, opaganib (ABC294640) is the most specific inhibitor available. It was shown to have no inhibitory effect on SphK1 up to 100 µM (French et al, J Pharmacol Experimental Exp Ther 2010; Neubauer HA and Pitson SM, The FEBS Journal 2013). In agreement, we found that PF543, the most specific SphK1 inhibitor, had no effect on AXL level (Figure S7F), unlike incubation with opaganib (Figure 6A and C), and that was confirmed in MCF10AF1F2 cells by the knock down of SphK2 with a specific siRNA (Figure 6B).
In the literature, depending on the cell lines, opaganib is used in vitro in the 10 to 60 µM range. Opaganib IC50 on recombinant SphK2 was established at 60 µM (French et al, J Pharmacol Experimental Exp Ther 2010). In our experiments, opaganib was used at a concentration of 50 µM, below the IC50 value, as previously done by Nichols’ group (Riento and al, PloS ONE, 2018). In most of our experiments (Figure 6, A, D, E-I, Figure S7D), opaganib was added for a maximum of 10 hours, which is shorter compared to what done in other studies (24-48 hours). Furthermore, it was shown that an opaganib concentration of 50 µM does not have any inhibitory effect in vitro on 20 protein kinases tested, including PKA, PKB, PKC, CDK, MAP-K, PDK1 and Src (French et al, J Pharmacol Experimental Exp Ther 2010).
In addition to inhibit SphK2, acting in a sphingosine-competitive manner, opaganib also was shown to act as an antagonist of estrogen receptor (ER), and inhibits ER-positive breast cancer tumor formation in vivo (Antoon JW et al, Endocrinology 2010). If Reviewer #3 is concerned about the possibility that the opaganib downstream effects we observed in our study might be explained by ER inhibition, we remind that we used cellular models that do not express ER. Indeed, the MDA-MB-231 cell line is a triple negative breast cancer cell line. MCF10A cells also do not express ER (Lane MA et al, Oncolgy Report, 1999,)** and our transcriptomic analysis (Table S1) did not reveal any increase in the expression of ER genes in MCF10AF1F2 cells in which flotillins are upregulated, thus eliminating a possible non-specific effect of opaganib in these cells.
In conclusion, we hope that these arguments help to convince Reviewer #3 that our experiments were performed in conditions where we carefully limited the possibility of opaganib off-target effects, on the basis of the currently available opaganib-related data from the literature.
We totally agree with Reviewer #3 that complementary experiments by downregulating SphK2 must be used. In agreement, we already downregulated SphK2 by siRNA in MCF10AF1F2 cells. This led to a significant decrease in AXL and ZEB1 expression. In the current revised version of the manuscript we have added data obtained with similar siRNA experiments performed in MDA-MB-231 cells (now Figure 6C). In agreement, we observed AXL and ZEB1 downregulation.
As shown below (Additional Figure 5) we recently obtained similar data in HS578T cells, showing that inhibiting SphK2 also affects AXL protein level in this triple negative breast cancer cell line (these data could be added in the manuscript).
ADDITIONAL FIGURE 5 CAN NOT BE ADDED BUT IS AVAILABLE UPON REQUEST
Additional figure 5: SphK2 inhibition decreases AXL level in HS578T cells. HS578T cells were incubated with opaganib (50µM, 10 hours) (A) or with siRNA Ctrl or siRNA SphK2 for 72 hours (B). Cell lysates were blotted with relevant antibodies against AXL, SphK2 and actin. The histograms show AXL level (normalized to actin) expressed as fold-increase compared with the control condition, and data are the mean ± SEM of 3 (A) and 4 (B) independent experiments.
Reviewer #3 also asks to use the siRNA approach on experiments shown in previous panels D-H (now panels E-I) of figure 6.
In complement to Figure 6D (now Figure 6E), experiments using a siRNA against SphK2 to show that “**AXL decrease upon SphK2 inhibition is not due to protein synthesis inhibition” are on-going and the obtained data could be added in the full revised version of our manuscript.
However, we are unfavorable to use a siRNA against SphK2, in addition to opaganib, in the experiments done to measure the effect of SphK2 inhibition on the rate of AXL internalization (previously in Figure 6E and F, now Figure 6F and G) and the level of AXL at the cell surface (previously in Figure 6G and H, now Figure 6H and I). Indeed, we carefully chose a short (4 hours) incubation with opaganib at the end of which the total cellular level of AXL was not yet decreased, allowing to measure unambiguously a defect in AXL endocytosis or a change in the level of AXL at the cell surface. We believe that it would be very difficult to achieve similar experiments using a siRNA against SphK2. It would require to determine the exact time after siRNA transfection leading to a sufficient SphK2 level reduction but in conditions where AXL level is still maintained. We think that due to the mosaic transfection efficiency, being able to precisely synchronize the effect of a siRNA at its beginning is impossible.
- Does overexpression of SphK2 reverse the effects of the SphK2 inhibitor? In a similar manner, does overexpression of SphK2 enhance stabilization of AXL?
To answer the first question, it is not clear for us how to test whether SphK2 overexpression can reverse the effects of the SphK2 inhibitor because the ectopically expressed SphK2 would also be sensitive to the inhibitor. This would require to overexpress a SphK2 mutant that is catalytically active but insensitive to the inhibitor, and to our knowledge, such a mutant does not exist.
Regarding the second question, we are currently generating a retroviral DNA construct allowing to overexpress SphK2 homogeneously in the cell population. Then we will test whether it further increases AXL level through its stabilization. This will be tested in cells upregulated for flotillin. As we showed in Figure 6 A and D (previously Figure 6 A and C) that AXL level depends on SphK2 activity only in cells that overexpress flotillins, we anticipate that there will be no impact in a cell line with a moderate level of flotillin. Results could be added in the fully revised manuscript.
- Although the authors suggest recruitment of SphK2 and formation of S1P in UFIT, there are no measurements of S1P. Also, there is no indication that SphK2 is activated despite the fact that ERK and AKT are activated in UFIT and are known to phosphorylate and activate SphK2. Is SphK2 that is recruited to flotillin phosphorylated?
To answer the first point raised by Reviewer#3, we recently performed, in collaboration with a lipidomic platform, a comparative analysis by quantitative mass-spectrometry of S1P levels between MCF10AmCh and MCF10AF1F2 cells. As we anticipated, the results show a 3,5-fold increase in S1P in MCF10AF1F2 cells compared with MCF10AmCh (Additional Figure 6). This data agrees with the fact that we found that the SphK2 catalytic activity is required for the UFIT pathway mediated AXL stabilization. This result is also in agreement with the study from the Nichols’ group which detect a decrease in S1P in cells in which flotillins were knocked out (Riento et al, PloS ONE, 2018). The results regarding the analysis of S1P level along with the complete methodology used will be added in the fully revised version of our manuscript.
ADDITIONAL FIGURE 6 CAN NOT BE ADDED BUT IS AVAILABLE UPON REQUEST
Additional figure 6: Upregulation of flotillins in MCF10A cells promotes an increase in the level of Sphingosine-1-phosphate. The level of sphingosine-1-phosphate was compared by quantitative mass-spectrometry analysis from three independent samples of MCF10AmCh and MCF10AF1F2 cells. The results are expressed in pmol equiv / 1 . 106 cells. The graph shows the value for each sample and the bar horizontal bars indicate the mean value for each condition.
Regarding the second point, we would like to clarify that we do not think that SphK2 interacts directly or indirectly with flotillins because SphK2 did not co-immunoprecipitate with flotillins (not shown). Thus, investigating by western blotting SphK2 phosphorylation status in flotillin immunoprecipitates is pointless. In theory, we could investigate the activity-related phosphorylation status of SphK2 associated with flotillin rich-membranes and endosomes. But this seems difficult to achieve because unfortunately, the only two commercially available antibodies against phosphorylated SphK2 are not described to work for immunofluorescence staining. One is against the Thr578 residue (https://www.abcam.com/sphk2-phospho-t578-antibody-ab215750.html), identified as phosphorylated downstream of ERK by Sarah Spiegel’s group (Hait et al, J Biol Chem, 2007). The second is designed to recognize specifically the phospho-Thr614 residue (https://www.abcam.com/sphk2-phospho-t614-antibody-ab111948.html), but this site has not been rigorously demonstrated to be phosphorylated downstream of AKT or ERK or to stimulate SphK2 activity. Thus, considering the lack of appropriate tools and considering that we already showed, using opaganib, that the catalytic activity of SphK2 is required for the UFIT pathway, we believe that investigating the phosphorylation status of SphK2 reflecting its activity in flotillin-positive vesicles will be complicated to achieve in a reasonable amount of time and we think that it will not bring a higher value to our present study.
To answer more broadly to the question “Is SphK2 recruited to flotillin phosphorylated?”, we anticipate that it could be the case at least on the Ser419 and Ser420 residues because Nakamura’s group demonstrated that the phosphorylation of these sites favors the nuclear export of SphK2 (Ding G et al, J Biol Chem, 2007). This group developed an antibody against these phospho-sites, potentially working by immunofluorescence. However, as it is unknown whether phosphorylation of these residues influences SphK2 activation status, we do not plan to perform immunofluorescence experiments with this tool (not available commercially) because the results would not address the Reviewer’s question.
- It should be determined whether the optogenetic system used to induce flotillin oligomerization also induces recruitment and activation of SphK2.
As we already have all the available tools, optogenetic experiments will be performed to answer this point and the results could be added to the fully revised version of our manuscript.
As suggested, we plan to perform experiments in which exogenous S1P will be added to cells with a moderate flotillin expression level to check whether it could recapitulate the effect of flotillin upregulation on AXL expression. Results could be added to the fully revised version of the manuscript.
However, our current results on the localization and the involvement of SphK2 suggest that the generation of S1P involved in the UFIT pathway occurs at the plasma membrane and in late endosomes. Because the exogenous S1P that will be added in the culture medium will not go through the plasma membrane, we anticipate that it could be insufficient to mimic all the mechanisms of the UFIT pathway. Its effect will be limited to the plasma membrane. In addition, these mechanisms are very likely based on a local concentration of S1P in some microdomains (at the plasma membrane and in intracellular membranes) scaffolded by flotillins. It will be very difficult to mimic such local concentration of S1P just by adding S1P to the cells.
We agree that identifying the S1P receptors involved would be of valuable interest for a better characterization of the UFIT pathway. However, we think that this is beyond the scope of our present study. Among the five known S1P receptors, we do not know if any could be involved in membrane remodeling at the plasma membrane to promote endocytosis. To our knowledge, involvement of S1P receptors in endocytosis has never been reported. However, based on the work by Nakamura’s group (Kajimoto et al, Nat Comm, 2013 and Kajimoto et al, J Biol Chem, 2018), the S1P1 and S1P3 receptors are involved in membrane remodeling and cargo sorting from the outer membrane of late endosomes (where flotillins accumulate in our cell models). We could hypothesize that these receptors are influenced by flotillins and are involved in the UFIT pathway. But we think that testing this hypothesis would be the subject of a distinct study.
At the plasma membrane, we totally agree that the effect of S1P could be mediated, as suggested by De Camilli’s group (Shen et al, Nat Cell Biol 2014), by the formation of tubular endocytic structure rich in sphingosine after acute cholesterol extraction. Reciprocally, in our cell models, upregulated flotillins, thanks to their ability to bind to sphingosine (demonstrated by Nichols’ group (Riento et al, PloS ONE, 2018)) and to oligomerize, could create sphingosine-rich membrane regions.
- There is a commercial antibody for endogenous SphK2 that can be used to validate and substantiate the data with GFP-SphK2. (F1000Res . 2016 Dec 6;5:2825. doi: 10.12688/f1000research.10336.2. eCollection 2016. Validation of commercially available sphingosine kinase 2 antibodies for use in immunoblotting, immunoprecipitation and immunofluorescence)
We thank Reviewer #3 for this suggestion and advice. Being able to detect the localization of endogenous SphK2 in late endosome would be valuable for our study. We already tried with no success with antibodies from Sigma and Cell Signaling Technology (not described to work in immunofluorescence experiments).
We will follow the advice from Reviewer #3 and test the anti-SphK2 antibody from ECM-Biosciences mentioned in the article by Neubauer and Pitson F1000 research, 2016. If we obtain interesting results, they will be included in the revised version of our manuscript.
However, in experiments using SphK2-GFP, we noticed that in live cells, the signal in late endosomes was completely lost after fixation using paraformaldehyde. Similarly, we also observed in live cells that NBD-Sphingosine, added in the culture medium, quickly accumulated in flotillin-positive late endosomes (Additional Figure 7, this data could be added in the fully revised version of the manuscript), but this accumulation was no longer detectable after fixation. Based on these observations, we believe that SphK2 recruitment to flotillin-positive late endosomes is highly labile probably because it mainly involves its interaction with sphingosine molecules that are enriched in these intracellular compartments. This is supported by our observation that addition of opaganib, characterized as a sphingosine competitive inhibitor, displaces SphK2-GFP from flotillin-positive late endosomes in live cells (Figure S7D). In addition, we showed that SphK2-Halo is more recruited in CD63-positive late endosomes in cells overexpressing flotillins (Figure 5E). This could be due to a higher concentration of sphingosine promoted by flotillins (that bind to sphingosine) accumulating in these compartments.
Thus, we will try the immunofluorescence staining of endogenous SphK2 using the recommended antibody, but it might be difficult to detect its presence in flotillin-rich late endosomes in fixed cells. The data could be added in the fully revised version of the manuscript.
ADDITIONAL FIGURE 7 CAN NOT BE ADDED BUT IS AVAILABLE UPON REQUEST
Additional figure 7: Visualization of NBD-sphingosine in flotillin-positive late endosomes. Live HS578T, MDA-MB-231 and MCF10AF1F2 cells expressing Flot1-mCherry were monitored by time lapse spinning disk confocal video-microscopy, 5 min after addition of fluorescent NBD-Sphingosine in the culture medium. On the right are shown still images corresponding to the boxed areas to illustrate the accumulation of NBD-sphingosine in virtually all flotillin-positive endosomes.
Reviewer #3 (Significance (Required)): This is an interesting paper. If the authors confirm the involvement of Sphk2 and mechanism of action of S1P, this would be an important contribution to the field.
Modifications done in the initial revised-version of our manuscript (at the time of the initial response). A full revised version will be provided after all the additional experiments asked by all the Reviewers will be achieved.
Revisions are highlighted in grey in the initial revised-version of the manuscript
1) Figure 1 has been modified and now includes results from a GSEA analysis as recommended by Reviewer #1. The texts of the corresponding legend and of the “Results” and “Methods” sections have been modified accordingly.
1) The Figure 2 version that was inserted in the manuscript was wrong because it was a copy of Figure S2. However, the correct Figure 2 was uploaded to the Review Commons website and accessible for the Reviewers. The correct Figure 2 is now inserted in the manuscript.
2) In the legend to panels C, E, F, J of Figure 2, the sentence: “The histograms show […] with control MCF10AmCh cells calculated from 4 independent experiments” was corrected to “The histograms show […] with control MCF10AmCh cells calculated from at least 4 independent experiments” because data shown in panel J are actually calculated from 8 independent experiments.
3) Figure 6 has been modified with the addition of panel C showing the effect of SphK2 downregulation by siRNA on AXL and ZEB1 level in MDA-MB-231 cells. The text has been modified accordingly.
4) In Figure 3 C, representative western blots have been added as asked by Reviewer #1.
5) In the Supplementary information section, the full clinicopathological characteristics of only 9 patients were indicated, whereas Figure S4 mentioned 37 patients. We corrected this mistake and now provide the characteristics of all patients.
6) In the sentence “Conversely, it induced ZEB 1 and 2 mRNA expression (Figures 1H and S1K) and ZEB1 protein expression (Figures 1I and S1L) (no anti-ZEB2 antibody is available)”, we removed “no anti-ZEB2 antibody is available”.
7) The sentence previously on line 995-997 "to our knowledge this is the first report to describe ligand-independent AXL stabilization..." has been modified to “**To our knowledge this is the first report to describe AXL stabilization following its endocytosis”
8) We are now referring to reference 18 (Planchon et al. J Cell Science, 2018) for the description of the cohort of 527 patients with breast cancer because this was missing.
-
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Referee #3
Evidence, reproducibility and clarity
This is an interesting and well written paper describing that upregulated flotillin promotes an endocytic pathway called upregulated flotillins-induced trafficking (UFIT) that mediates AXL endocytosis and allows its stabilization. Consequently, stabilized AXL in these flotillin-positive late endosomes enhances activation of oncogenic signaling pathways that promotes EMT. The authors suggest that Flotillin upregulation-induced AXL stabilization requires the activity of SphK2. However, this latter point is not supported by the data and further studies are needed to support this important conclusion.
Major concerns:
- Most of the conclusions are based on effects of high concentrations (50 uM) of an ill-defined SphK2 inhibitor. The experiment described in Figure 6C-H need to be confirmed by downregulation of SphK2.
- Does overexpression of SphK2 reverse the effects of the SphK2 inhibitor? In a similar manner, does overexpression of SphK2 enhance stabilization of AXL?
- Although the authors suggest recruitment of SphK2 and formation of S1P in UFIT, there are no measurements of S1P. Also, there is no indication that SphK2 is activated despite the fact that ERK and AKT are activated in UFIT and are known to phosphorylate and activate SphK2. Is SphK2 that is recruited to flotillin phosphorylated?
- It should be determined whether the optogenetic system used to induce flotillin oligomerization also induces recruitment and activation of SphK2.
- Most importantly, it has not been established that the effects are mediated by S1P. Does addition of S1P enhance stabilization of AXL? Are the effects of S1P mediated by a S1P receptor? If so, which S1P receptor? There are several specific agonists and antagonists of S1PRs that can be utilized to answer this question. It's also possible that the effects of S1P are mediated by intracellular actions as were suggested by the De Camilli group (Nat Cell Biol. 2014 Jul;16(7):652-62).
- There is a commercial antibody for endogenous SphK2 that can be used to validate and substantiate the data with GFP-SphK2. (F1000Res . 2016 Dec 6;5:2825. doi: 10.12688/f1000research.10336.2. eCollection 2016. Validation of commercially available sphingosine kinase 2 antibodies for use in immunoblotting, immunoprecipitation and immunofluorescence)
Significance
This is an interesting paper. If the authors confirm the involvement of Sphk2 and mechanism of action of S1P, this would be an important contribution to the field.
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Referee #2
Evidence, reproducibility and clarity
Genest and co-authors present in this paper new fascinating evidence on how intracellular trafficking can modulate oncogenic sigalling.
First of all, they show how overexpression of Flotillin1 and 2 in non-cancerous breast lines can induce a strong reprogramming towards a EMT phenotype. They analyse mRNA and protein expression, intracellular distribution of activated proteins, cell phenotypes to demonstrate a strong activation of oncogenic signalling pathways. They then identify AXL as a key player in this process and show how this protein is stabilised upon Flotillin expression. The authors use an amazing variety of approaches to study the endocytosis and the trafficking of endogenous, GFP-tagged, Halo-tagged and Myc-tagged AXL in different cell lines and their data are strong and very convincing, the images are of very high quality and the analysis rigorous. Their data strongly support the hypothesis that high Flotillin levels triggers AXL endocytosis and accumulation in non-degradative late endosomes where signalling remains active. The authors then show how SphK2 has a key role in AXL stabilisation, it colocalises with Flotillin, AXL and CD63 and its activity (which they block by using inhibitors or siRNA) is necessary for flotillin-induced AXL stabilisation and EMT induction.
The paper is extremely well written, the data flow logically and they are appropriately presented and analysed.
I don't have any major comment and I believe the paper is suitable for publication.
I have only some minor comments/questions:
1) did the authors try to colocalise AXL with endogenous Flotillin in MDA-MB-231 cells? They could use the antibodies used in Fig S1B. Of note, the authors have shown it in luminal tumours in Fig S4C.
2) In Fig6G, it appears that AXL-Flotillin colocalization is lost upon SphK2 inhibition. Is this the case? It could be that the correct lipids are necessary for the formation of Flotillin-positive internalisation domains and this could be very interesting and reinforce the model proposed in the paper.
3) I would remove the sentence on line 995-997 "to our knowledge this is the first report to describe ligand-independent AXL stabilization..." as the cells are not serum starved in all experiments and animal serum can contain variable amounts of the ligand GAS6.
Please note that the authors don't have to necessarily address comments 1-2, their paper is already very rich in convincing data.
Significance
AXL is a major oncogene that promotes EMT in a variety of tumour types. Understanding how its signalling can be triggered by endocytic pathways even in cells that are non-cancerous is very important and of high significance for the cancer field and the trafficking community.
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Referee #1
Evidence, reproducibility and clarity
The paper by Genest et al. describes the effect of flotillins and sphingosine kinase 2 to stabilize AXL as a mechanism to promote epithelial-mesenchymal transition in breast (cancer) cells. The potential role of vesicles trafficking EMT-promoting proteins is of high interest in the field, also for exploring new opportunities of pharmacological targeting. However, the paper fails to convincingly demonstrate that the proposed mechanism is of real importance to support or promote EMT for the following main reasons:
1) The role of flotillins is studied only by overexpression and in the context of non-cancerous MCF10A cells, while breast cancer cells of epithelial-like origin are not analyzed. This is contrast with the purpose of the paper (see abstract, introduction, patients' data) which is to study tumors and EMT. Effect of shRNAs is also not reported, making it difficult to estimate the importance on the EMT phenotype. Then, alteration of EMT should be concluded also from other non-genetic functional parameters, not just by markers. For instance: was morphology of the cells changed? Was cell migration affected with F1F2?
2) AXL up-regulation is not very strong (2-fold). What is unclear is if the minimal AXL increase due to F1F2 really really provides a significant contribution to the EMT phenotype (as the authors conclude). The siRNA experiment knocks down all AXL, not just the F1F2-induced levels, making it difficult to estimate the real effect of the mechanism proposed. Why didn't the author focus on EphA4 (or to a lesser extent ALK), which showed better regulation?
3) The conclusions of the manuscript are contradicted by the reported clinical data. In Figure S4 the authors clearly observe co-expression of Flotillin 1 and AXL prevalently in luminal breast cancers, which is the subtype known to not be driven by EMT. This evidence already indicates that this (otherwise interesting) mechanism is not relevant to EMT in breast cancer. So, the conclusions are not supported by the data, and the experimental setup and model chosen are not appropriate to generalize the findings to cancer.
Minor (here the most important):
4) The point of the Figure 2 is not clear. Why this part should have such a central role in the story? The entire data presented are not followed up in the rest of the paper. Moreover, in some cases upregulations also questionably significant (like RAS and STAT3 are not even 2 fold). Moreover, the error bars are so small that it seems unrealistic that the plots indicate three independent experiments.
5) More robust statistical analysis should be provided in the Figure 1 to support that EMT is suppressed with F1F2 overexpression. For instance a more standard GSEA on hallmark signatures.
6) In Figure 3 E-Cadherin is rescued with siAXL in the IF but not in the western blot.
7) Some sentences require clarifications. The authors should be more clear on why ZEB2 antibody was not available or what they mean with "Unfortunately the available tools..".
8) Western blot from the CHX experiment should be shown, at least in the supplements. Again, the standard deviation in this experiment is minimal, was this really an average of three independent experiments (and not three western on the same lysates)?
9) All conclusions are derived from one single cells MCF10a. NMuMG cells are shown at the beginning but not used for the rest of the paper. Anyway, if this wants to be a cancer research paper, then cancer cells needs to be used.
10) The methods section contains inconsistent data about patients' samples (9 are indicated, but the Figure S4 features 37). Then, where those other 527 come from?
11) Some figures do not match with the legends or with the description in the text. It has not been easy to review this paper.
Significance
I am a cancer biologist working on EMT.
Referee Cross-commenting
I have nothing to comment on other's reviews.
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Referee #3
Evidence, reproducibility and clarity
Recommendation: Publish after revisions
Duart and colleagues have put forth a manuscript detailing the under-appreciated effect of intrahelical salt bridge formation to the insertion transmembrane helices. Utilizing an in vitro and in vivo applicable construct of vehicle protein leader peptidase (Lep) from Escherichia coli, the authors were able to use glycosylation patterns as a way to quantify the apparent free energy of membrane insertion for multiple transmembrane helices. These results have demonstrated the importance of taking salt bridge formation into account when developing membrane protein prediction tools; however, prior to publication, further analyses would be beneficial for supporting their quantitative conclusions.
Major Comments:
- It would be helpful if the authors detailed their process in deciding which of the 136 potential salt bridge-containing helices were chosen for further investigations.
- Considering the data presented in Fig. 3c, it may be useful to also include charged pair mutations in the i, i+3 positions in the analyses of helix G and helix A, as these positions are the most likely to form salt bridges. This would act as a useful positive control, to see if the mutations would improve the insertion of the sequence.
- Page 14, Line 255: Authors state "The salt bridge contributes approximately ~0.5 kcal/mol to the apparent experimental free energy of membrane insertion." Can this change in apparent free energy be attributed completely to the mutation? Are there any potential interactions between the inserted helix and the natural H2 transmembrane sequence of Lep that could be changing with the various mutations?
- It is promising to see these results in the context of the Lep protein, but the authors should consider the effect these salt bridges may have in the context of the full protein. Creating mutants of Halorhodopsin or calcium ATPase would determine the impact of potential salt bridge disruption on protein folding, which would provide some context on the functional consequences of these mutations.
- Authors have presented a strong argument for the inclusion of potential salt bridge formation in the prediction of transmembrane helices; however, they have not detailed the necessary steps for developing a new system. It would be encouraging to see recommendations on the next steps towards better prediction software.
Minor comments:
- Page 8, Line 118: Authors state "Our results showed a tendency to better insertion when charge pairs were placed in positions (i, i+1; i, i+3; i, i+4) that are permissive with salt bridge formation (Fig. 1c), actually an effect not observed in the predictions (Fig. 1b)." It is important to clarify that this "better" insertion in Fig. 1c is compared to each respective predicted value in Fig. 1b. Currently, it reads as if the authors are suggesting the introduction of the charged pair residues is helping the insertion of the unaltered L4/A15 sequence.
- Figure 1a: Add cytoplasmic and lumen identifiers for clarity.
- Figure 3b: Slashes for "Opp charge" and "Same charge" in the legend appear to be reversed according to the values presented in Table 2.
Significance
This paper increases our understanding of salt bridges in membrane protein structure and function, as performed systematically by a lab with major expertise in this research area.
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Referee #2
Evidence, reproducibility and clarity
As the title states, Duart et al. have examined the energetic cost of the translocon-assisted insertion of TM helices containing salt bridges into membranes. The paper has three parts: (1) model studies using the methods of Hessa et al. (12,13), (2) statistical analysis of salt bridges in membrane proteins of known 3D structure, and (3) Hessa et al. measurements of selected i,i+4 salt-bridge containing TM helices from halorhodopsin (PDB ID = 3QBG) and calcium ATPase (1SU4). The major overall conclusion is that for i,i+4 salt bridges yield a more favorable insertion free energy of about 0.5 to 0.7 kcal/mol.
The subject of the paper is broadly interesting, but it suffers from several problems that must be addressed before it can be considered seriously for publication. The comments below are described in terms of the three parts.
(1) Figure 1b reports tabular values of predicted Hessa et al. DG values for sequences that contain K, D, or K & D substitutions in a parent L4A15 parent sequence, which has a favorable DG of about -0.5 kcal/mol. For all of the other sequences, DG is predicted to be unfavorable 1.4 kcal/mol to 3.5 kcal/mol. Figure 1c presents triplicate experimental measurements of DG for the sequences in Figure 1b shown as bar graphs. All of the sequences yield unfavorable DG values of about +0.2 kcal/mol except for the parent sequence that has a favorable value close to the predicted value.
There are several problems with these data and their presentation. Fig. 1b should also include the measured DGs with standard deviations in addition to the predicted values. In Fig. 1c, the positive values are plotted on different scale than the sole negative value. This causes the authors to insert a break in the bar representing the sole negative value. The bars are color coded in a mysterious way that is not clearly described in the figure legend. In any case, the measured DG values are all about the same.
A fundamental problem with the measurements is that the method of Hessa et al (12) should have been adhered to rigidly. As those authors noted "The quantification [of DG values]is maximally sensitive for H-segments with DGapp values close to zero (p < 0.5 in Fig. 1d); therefore, for each kind of residue we balanced the contribution from the central residue by varying the number of Leu residues until an H-segment with DG in the range -1.2 to 1.2 kcal/mol was found." The measurements reported Fig. 1b and 1c are far outside the maximum sensitivity range. The Western blots upon which the numbers are based should have been included (perhaps as an appendix).
(2) The statical analysis seems fine and is useful.
(3) Fig.4, halorhodopsin helix G measurements. The table of Fig. 4a should be expanded to include both in vitro (panel e) and in vivo data (panel f). It is not entirely clear where the values given in the table are from, but presumably from the in vitro data (panel e). Fig. 5, calcium ATPase helix A. Comments similar to those regarding Fig. 4 apply. The division of the long helix into a short greasy one and longer one carrying more charges is interesting, but it seems to add little to the main intent of the paper to assess the thermodynamic properties of helices containing salt-bridges.
Overall, the paper would be stronger if it focused mostly on the part (1) experiments to arrive at definitive answer to the energetics of salt-bridge insertion. As it stands, it is a smash up of ideas and experiments.
Significance
Surprisingly,there have been no reported measurements that I am aware that examine the energetic cost of inserting TM helices containing salt bridge into membranes. This paper is a start in that direction.
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Referee #1
Evidence, reproducibility and clarity
Summary:
In the manuscript „Intra-helical salt bridge contribution to membrane protein insertion" the authors investigate the effect of salt bridge formation between positively and negatively charged amino acids on the insertion behavior of α-helical protein segments into the membrane. Generally it is believed that polar or even charged residues prevent stable membrane insertion of α-helical protein segments, but some of these authors had already shown in a previous paper that such residues are more frequent than expected in transmembrane helices. In the current study, the authors investigate in detail the role of intra-helical salt bridge formation on stable membrane insertion. Using an in vitro membrane insertion assay based on the E. coli leader peptidase (Lep) protein, they found better membrane insertion for helical segments with opposite charge pairs placed at positions compatible with intra-helical salt bridge formation (positions i→i+1; i→i+3 and i→i+4). Furthermore, the authors performed a database screen which revealed that oppositely charged residues are overrepresented at these positions. Finally they picked two candidate membrane proteins from the database (Halorhodopsin and calcium ATPase 1) and proved the presence of an intra-helical salt bridge and determined the contribution of the salt bridge to the apparent free energy of membrane insertion (ΔGapp), which was in the range of 0,5-0,7 kcal/mol.
Major comments
- It seems that the data in Fig. 3b has been mixed up, making it difficult to judge the conclusions. The bars with forward slash seem to represent the "same charge" data and the bars with backward slash seem to represent the "opposite charge" data (exactly contrary to the figure legend). In general the forward and backward slash representation is not easily distinguishable, and for the position i+4 both bars contain a forward slash (making it impossible to discriminate same and opposite charge). Please use filled and unfilled bars instead. Furthermore the bar diagram in Fig. 3a is stacked for opposite and same charge, whereas in Fig. 3b the respective bars are placed next to each other. Additionally the label of the y-axis in Fig. 3c is misleading, as it is not the "Frac. of opp. charged pairs" but the fraction of oppositely charged pairs that form salt bridges.
- The authors don´t give details no how the log odds ratios and the respective p-values have been determined. Please include this in the Materials and Methods section. What does a p-value of 0.00e+00 mean (see Table 2, Spacing: +3, "All Log odds")?
- What is the proof that for the isolated helix A from the calcium ATPase 1 the membrane embedded part is identical to the full-length protein? The authors investigated two different helix A peptides, the full-length helix ranging from L49-F78, and one short fragment ranging from L49-A69 containing the more hydrophilic N-terminal region, which is the membrane-embedded region in the full-length protein. The authors state: "In contrast, when only the membrane-embedded sequence was included, the Lep chimera was mainly doubly-glycosylated (Fig. 5c, lane 3), suggesting that helix A is properly inserted when the full helical sequence is present." In my opinion this conclusion cannot be drawn from the data presented. The authors used an isolated helical segment, so in my opinion it is much more likely that the isolated full-length helix inserted via its hydrophobic C-terminal part (L60-F78) into the membrane. The authors themselves state in their manuscript: "It has been previously shown that the position in the membrane of TM helices in protein folded structures does not always correspond to the thermodynamically favored positions in the membrane of the isolated helices." Also the i→i+5 mutant points into that direction, because the effect of disturbing the intra-helical salt bridge for the helix A is much less pronounced compared to the similar data in Fig. 4f for the Halorhodopsin protein. In my opinion this shows that most probably only one charged residue (R63) is embedded inside the membrane (with a membrane embedded part of L60-F78).
Minor comments:
- line 151: ",see Figure 2)" Typo: Bracket missing.
- line 172: "Other known structural features can also be hinted at, including aromatic ring stacking by His-Trp pair [20] at i→i+6." Please give some more examples of important structural features of membrane proteins, which can be seen in your analysis (e.g. I think that also the glycine zipper can be seen in the i→i+4 data set).
- line 255: "The salt bridge contributes approximately ~0,5 kcal/mol to the apparent experimental free energy of membrane insertion." Please explain that this value was derived from the comparison of the ΔGexp between the wt and the i→i+5 mutant. Please comment also on the large difference between the predicted (ΔGpred) and the experimental values (ΔGexp), even if no salt-bridge is involved (e.g. for the DD mutant).
- line 348: "Asp-Lys pairs at position i, i+4 and Glu-Lys pairs at position i→ i+3 are the most prevalent as seen previously in Figure 2. They are both among the most prevalent oppositely charged pairs and the charged pairs that form the highest number of salt bridges in membrane protein structures. This is in stark contrast to Glu-Arg pair at position i→ i+1 that although as frequent in pairs as Asp-Lys and Glu-Lys at positions i→i+4 and i→i+3 respectively, only form salt bridges in one-fourth of the cases." Fig. 2 shows that each charge pair has a different prevalence depending on the order (e.g. Asp-Lys and Lys-Asp pairs). I think for this statement the sum of both prevalences should be taken into account, and as the sum is not easy discernible from Fig. 2, it would help to include a table containing the sums. Furthermore, it would be good to refer also to Fig. 3, which also contains a part of the discussed data.
- line 402: "c-myc tag (Glu-Gln-Lys-Leu-Ile-Ser-Glu-Glu-Asp-Leu, EQKLISEEDL) was added in Ct in hanging with de PCR primer before cloning." Please revise the sentence and I think the one letter code for the c-myc tag is sufficient (please correct this also in line 428).
- line 420: "A region's total ΔG is the sum of these individual scores weighted on where in the region the residue, a residue in the middle of the helix has a higher weight than residues at the ends." Please revise the sentence, the meaning is unclear.
- line 436: "Total protein was quantified and equal amounts of protein submitted to Endo H treatment or mock-treated, followed by SDS-PAGE analysis and transferred into a PVDF transfer membrane (ThermoFisher Scientific)." Please revise the sentence.
- line 498: "Topological files with sequence and membrane topology are created with the help of the RCSB secondary structure file and only membranes annotated as pure α-helices were retained." I assume that the description contains a typo (membranes annotated as pure α-helices?)
- line 507: typo "..., but we did not clustered the proteins" 14: line 560: "The individual value of each experiment in represented by a solid dot being represented as a green square the experimental ΔG value for the L4/A15 sequence from [2]." Please revise the sentence. 15: line 562: "The wt and simple mutants are shown in white bars." Typo: single mutants 16: line 563: "Charges at compatible distances with salt bridge formation (i→i+1; i→i+3; and i→i+4) are shown in yellow. Not compatible distances with salt bridge formation (i→i+2; and i→i+5) are shown in dark gray. Compatible distances but not compatible amino acid pair (i, i+4 DD pair) is shown in clear gray." The given colors don´t match with the figure (i→i+1 = brown; i→i+3 = orange; i→i+4 = yellow and i→i+4 DD pair = white) 17: line 597: "The different monomers are shown in transparent blue, purple and indigo." The different colors are hardly distinguishable in the figure. 18: Figure 4a: The table could be simplified. I think the column "charges" can be removed, as it contains not really charges and the names of the peptides already contain the same information. The column "Å" contains only a value for the wt (and not for the DK i,i+5 mutant) and as the distance for the wt is also given in Fig. 4g, this column can be also removed.
- Fig. 4f: The marker lane is hardly visible (completely dark lane)
- Fig. 5b: The column "Å" contains only values for the wt sequences (long and short). See also comment 18.
- Fig 5d: Why is in the SDS gel a mass shift between the wt and the i→i+5 mutant visible, even though the peptide mass is equal.
- There are several changes of font type or format changes (e.g. line 210-214). Please correct this.
Significance
As a structural biologist with a focus on membrane-proteins, I understand that the study is concerned on intra-helical salt bridges, but the implications of inter-helical salt bridges should also be discussed, at least in the introduction or outlook. The authors propose that their results are important for the improvement of membrane protein topology prediction methods, so for this aim it is also necessary to take any potential inter-helical salt bridges into account. In this context, it would be relevant to point point out that there even exist extended rows of salt bridges between transmembrane segments (charge-zippers), which serve an important structural element in several membrane proteins.
The article is well written and most of the conclusions drawn from the experimental results are convincing. I agree with the authors that their results are relevant for future improvement of membrane protein topology prediction software, which so far does not take the possibility of salt bridge formation into account. Therefore, I recommend publication after clarification/revision of the abovementioned points.
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Reply to the reviewers
We thank the three reviewers for their helpful and valuable comments. We plan to address their criticisms in a revised manuscript and hope that our manuscript will then be significantly improved.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
The authors have presented a very interesting and compelling set of data regarding the impact of conditional deletion of the only known pathway allowing the uptake of pyruvate into mitochondria. The paper comprises two interwoven stories that are both important. The first is the remarkable finding that the majority of excitatory neurons in the cortex (i.e. those under the influence of the CaMKII promoter) show remarkable metabolic flexibility as they tolerate elimination of pyruvate oxidation, considered the major supplier of ATP in neurons. The data on this seem clear although the authors did not delve into the potential mechanisms of metabolic compensation that likely occurs. Instead they examined whether there was some mal-adaptive compensation and they found clear evidence of this: in the absence of MPC activity the mice are much more prone to epileptic seizures, unveiled experimentally by relatively standard protocols (kindling). The authors present largely very convincing evidence that this mal-adaptive compensation in turn ends up decreasing the activity of KV7.2/7.3 channels whose job is normally to limit runaway repetitive firing by mediating an hyperpolarizing K+ efflux following an action potential. This channel, put on the map as it was one of the downstream targets modulated by cholinergic metabotropic activation, is also know known to be controlled by Calmodulin and therefore cytosolic Ca levels. Overall, I think at its core this manuscript is interesting and important. There however several weaknesses, I fear, will diminish the impact on the eventual readership. If these points can be addressed, it will strengthen the longevity of these findings:
1) It is puzzling why the authors resorted to using shRNA-mediated KD of MPC1 for some of the in vitro studies when they have gone to the trouble of making a floxed CRE-dependent mouse. Primary cells (e.g. Fig 1) or organotypic cultures (Fig. 6) from these mice would have made a more consistent set of starting conditions to compare data across the manuscript. As there viruses expressing the CRE recombinase are widely available this could have been used on mice simply harboring the floxed gene it they are worried about waiting for the expression of the CaMKII promoter for in-vitro conditions.
This is indeed a good point. Indeed initially, when we started these experiments, we tried to use viruses expressing the CRE recombinase in cultured neurons from mice harboring the floxed gene as proposed by the reviewer. However, for reasons that we do not fully understand, the use of AAVs or lentiviruses expressing the CRE was found to be deleterious for the cultured neurons. In view of this toxicity we tried using TAT-CRE recombinase, a recombinant cell-permeant fusion recombinase, which we added directly to the medium. However, this strategy proved to be poorly efficient. We finally used cultures of Cre-floxed neurons in which we tried to knockout MPC1 gene using 4-hydroxytamoxifen in the culture medium. However, we did not obtain satisfying results because, as previously reported, cortical neurons grow poorly in the presence of 4-hydroxytamoxifen (Nichols et al., Cell Death and Disease, 2018. https://doi.org/10.1038/s41419-018-0607-9). For these reasons we turned to the shRNA strategy and to the use of 3 small molecule inhibitors of the MPC each with different chemical structures. Both the RNA interference and the pharmacological approaches gave similar results, reinforcing our confidence in the specificity of the results, and the unlikelihood of off-target effects.
2) The data in Figure 5 gets a little less convincing as using extracellular glutamate to drive Ca elevations is so non-physiological that the results might really be distorted by the participation of something irrelevant to the story, even though it supports the overall interpretation for a role of Ca/CaM in the control of the channel. Similarly, the use of RU360 should be done with caution. The drug, although a useful antagonist of MCU in purified mitochondria, is famously finicky with respect to its ability to cross membranes and could well have off target impact. A much cleaner experiment would be to suppress the expression of MCU via KD. Presumably in the MPC-deficient neurons, this would have minimal impact on Ca signals. Given the frequent ambiguity associated with interpreting pharmacological results, coupled to the central importance of this finding in interpreting the entire paper, I think carrying out experiments with molecular genetic manipulation of MCU is warranted.
The main point of this figure is to study the capacity of MPC1 KO neurons to handle intracellular calcium increase and to regulate calcium homeostasis. To this end, we used strategies described to acutely increase cytosolic calcium, either through membrane depolarization with KCl (Rienecker et al., ASN Neuro. 2020. https://doi.org/10.1177/1759091420974807) or through activation of glutamate receptors using glutamate (For example see Wong, Vis Neurosci, 1995 : DOI: 10.1017/s0952523800009469). It is important to mention that the concentration of glutamate used in our experiments (10 microM for 2 min) is well below the concentration normally used to induce excitotoxicity (100-500 microM for 30min). The fact that both stimulations provided similar results and clearly indicated a defect in the clearance of cytosolic calcium in MPC-deficent neurons.
Regarding the concern with RU360, we are aware of the problems with plasma membrane permeability associated with this compound, and for this reason we included a membrane permeabilizer (0.02% pluronic acid) to facilitate its entry into the cell. This was indicated in the Material and Methods section (line 585) as well as in the figure legend (line 948). In order to clarify this methodology, we will add this information in the main text. It should be noted that this concern would not apply to the electrophysiogical experiments, since in this case the compound was injected directly into the cell. We would like to add that we chose to inhibit the MCU using a chemical inhibitor rather than a shRNA because of the well known difficulty in obtaining a complete loss of function of the MCU using RNA interference (Nichols et al., Cell Death and Disease, 2018. https://doi.org/10.1038/s41419-018-0607-9). Nevertheless, as recommended by the reviewer, we will attempt to downregulate the expression of MCU using shRNA.
3) The authors have not really made clear in this paper whether the ability to suppress the phenotype of the MPC deficiency with ketones is really related to a providing TCA cycle support or instead a pharmacological impact on non-TCA related targets (such as the Kv7.2/7.3 channels). Presumably the use of other ketones might circumvent this. The action of ketone bodies has been a topic of considerable interest in neuroscience, given the clinical relevance for childhood epilepsies. Previous studies for example have argued for direct inhibition of the vesicular glutamate transporter (Juge et al. Neuron 2010). The use of other ketones (acetoacetate) would narrow down the interpretations of the data.
Our results point to 2 two possible mechanisms of ketone bodies: i) providing acetyl-CoA to the Krebs cycle, thereby stimulating OXPHOS and ii) direct action of 3-beta hydroxybutyrate on the activity of Kv7/7.3 channels. The reviewer is asking whether, in addition to 3-beta hydroxybutyrate, other ketone bodies, acetone or acetoacetate, may display antiepileptic activity, which would probably indicate that providing substrates to the TCA cycle is sufficient to prevent neuron-intrinsic hyperactivity and seizures. We agree that this in an interesting question and we will now test the effect of acetoacetate on PTZ-induced seizures in MPC KO mice.
**other**
1) In vitro - scramble controls only serve to demonstrate there is no general effect of treating cells with shRNAs, but do not address if there is an off-target effect. The most convincing thing here would be to have an shRNA-insensitive variant that rescues.
We have used 2 different shRNAs and 3 chemically unrelated inhibitors of the MPC and in all cases we obtained similar results. Therefore, we think that it is unlikely that the effects we observe are due to an off-target activity. The experiment proposed by the reviewer is interesting but extremely difficult. The idea would be to reintroduce a shRNA-insensitive MPC1 into MPC1-deficient neurons treated with shRNA. This is difficult as it is known that the expression level of MPC1 needs to be matched to that of MPC2, otherwise it leads to depolarization of the mitochondria. Obtaining the right level of MPC1 would be extremely difficult to achieve in practice.
2) Does rescuing CaMK binding to KCNQ channels rescue the phenotypes?
The question raised by the Reviewer implies that CaM is not constitutively bound to KCNQ channels, which is a matter of debate. As we pointed out in the discussion, ‘Intracellular calcium decreases CaM-mediated KCNQ channel activity (32, 36) by detaching CaM from the channel or by inducing changes in configuration of the calmodulin-KCNQ channel complex (36).’ The CaM-KCNQ tethering is also described in a review by Alaimo and Villaroel, 2018 (doi:10.3390/biom80300579): ‘[…] CaM was first defined as an integral subunit constitutively tethered to the C-terminal region of Kv7.2/3 channels since Kv7.2 mutants that were deficient in CaM binding were unable to generate measurable currents [5,21]. However, this model has been questioned since Kv7.2 channels, carrying a hB mutation [40] or Kv7.4 hA mutated channels [41] that do not bind CaM, can still reach the plasma membrane and are functional.’
When considering to manipulate CaM binding to KCNQ, it should also be considered that previous studies on this matter have mainly worked with heterologous systems and through genetic manipulations of CaM (by expression of a dominant negative or by overexpression of CaM) or of the KCNQ binding motif.
Based on both theoretical and practical issues, we, thus, believe that it is not feasible to implement a straightforward approach that would be compatible with our mouse model.
An alternative, indirect approach, as indicated by Reviewer #3, would be to test the effect of Ca2+ chelators. Although this is likely to introduce confounding effects through the inhibition of other Ca2+-dependent channels, we propose to focus on trying this option and assess whether a XE991-sensitive component will be unmasked in MPC1 deficient cells.
3) As the authors imply that BHB activates KCNQ channels, showing this directly in their prep would provide some convincing data. If this is true, why doesn't BHB increase firing rate of WT neurons?
Activation of KCNQ channels is expected to reduce (not increase) neuronal firing. When exposed to BHB, we indeed found that WT cells also show a trend towards decreased excitability (p=0.08). We will report this trend in the revised figure 5F. Given that KCNQ channels are already available to be recruited upon repetitive firing in WT cells (to a larger extent as compared to KO, as indicated by our data with XE991) it is conceivable that a further potentiating effect of BHB at the concentration used for ex vivo recordings (2 mM) will be limited.
4) How does the anti-epileptic effects of ketones in this study relate to previous reports of regulation of KATP channels? One of main concerns is that ketones might have a parallel anti-epileptic effect in the MPC1 KO mice that is unrelated to the mechanism proposed here.
The ketogenic diet is likely to exert several effects including disruption of glutamatergic synaptic transmission, inhibition of glycolysis, and activation of ATP-sensitive potassium channels as pointed out by the reviewer. We do not exclude that inhibition of the MPC could also have an impact on the KATP channels and we are currently exploring this possibility. However, such work to dissect the potential implication of the KATP channels would go well beyond the scope of the present paper. Nevertheless, we will plan to certainly raise this important possibility in the discussion.
**Minor comments:**
1- What is the MPC1 KO efficiency in CaMK neurons? The western blot in 2c is from the whole cortex and therefore does not show that.
This is indeed a good comment, however, please note that the estimation of MPC1 KO efficiency has also been evaluated in synaptosomes isolated from MPC1 KO cortices. These structures are mainly isolated from neurons (Carlin et al., JCB, 1980. 10.1083/jcb.86.3.831). As shown in figure 2C, these synaptosomes are massively enriched for CamKII and contain less astrocytic marker GFAP in comparison to the whole cortex. The amount of MPC1 in the synaptosomes prepared from the KO animals is strongly decreased. Nevertheless, as recommended by the reviewer, we plan to quantify the efficiency of the KO by performing a double immunostaining for MPC1 and a specific marker for neurons.
2- Mitochondrial Ca2+ levels are not measured directly, for which there are many tools. This is needed to demonstrate definitively that there is a defect in Ca2+ handling."
The reviewer raised an important point and we plan to monitor the levels of mitochondrial calcium in MPC-deficient neurons using the mito-Aequorin, a luminescent quantitative probe targeted to mitochondria (Granatiero et al., Cold Spring Harb. Protoc. 2014. 10.1101/pdb.top066118)
Reviewer #1 (Significance (Required)):
see above.
**Referee Cross-commenting**
It seems we are in reasonable agreement about the pros & cons of the manuscript. I agree that alternative approaches to RU360 are warranted.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
De la Rossa and colleagues examined the consequences of conditionally knocking out MPC1,a subunit of the mitochondrial pyruvate carrier. They found that despite decreased levels of oxidative phosphorylation in excitatory neurons, phenotypically these conditional knockout mice were normal at rest. However, when challenged by inhibition of GABA neurotransmission, these animals developed severe seizure activity and expired. These authors then showed that neurons with an absence of MPC1 were hyperexcitable in part through abnormal calcium homeostasis, which was associated with a reduction in M-type inhibitory potassium channel activity. Intriguingly, the ketogenic diet and the major ketone body beta-hydroxybutyrate were able to reverse these changes.
This is a carefully conducted research study that reveals cell type-specific alterations of MPC1 deletion and functional consequences. The study design was logical and involved an exhaustive array of methodologies. The manuscript was generally well written and organized, and there are no major concerns. This study shows a direct causal relationship between impaired bioenergetics at the level of mitochondrial, and subsequent behavioral seizures, and is perhaps the most direct demonstration to date that an intrinsic disturbance of metabolic function can result in seizure activity (through changes in calcium regulation and impairment of ion channel activity). This will be an important contribution to the scientific literature.
**MINOR:**
- Page 4, line 86: Would recommend changing "paroxystic" to "paroxysmal" (the latter which is a more recognized term). We will make the change.
Page 5, line 124: recommend including the concentration of beta-hydroxybutyrate used when first mentioned. In general, concentration and dose information were difficult to find, as well as route of administration (for kainate, page 7, line 175). This type of information was not conveniently presented.
We will follow the reviewer’s recommendation.
Page 5, line 128: "both overcomed" is awkward. Would recommend using "both reversed".
We fully agree and will make the change in the revised manuscript.
Page 8, line 193: the authors probably meant "astro-MPC1-WT mice", not "neuro-MPC1-WT mice".
Thank you for the acurate look. This will be changed.
Page 12, lines 280-282: the authors might want to mention that chronic exposure of BHB might reduce the hyperexcitability of neuro-MPC1-KO mice.
This point could indeed be discussed.
Please review entire manuscript and use consistent tense. For example, on page 13, line 309, to maintain the past tense, it should read "We first assessed whether..."
Thanks for the recommendation.
Page 13, line 318: the authors used 10 mM BHB when examining calcium levels, but they earlier used 2 mM. They need to explain why they used a different concentration; and 2 vs 10 mM are quite different.
The reviewer makes a valid point. When we performed the in vitro experiments, we used 10 mM BHB, which is slightly higher than the amount of ketone bodies measured in the blood of mice fed on a ketogenic diet for 2 days (Supplementary figure 4). This concentration of BHB has also been used by others (see for example: Izumi et al., JCI 1998, 101:1121-1132). Later on, when electrophysiology experiments were performed, the person in charge of these experiments followed a previously published protocol by Yellen and colleagues, in which the authors had used 2 mM BHB (Ma et al., J. Neurosci 2007,27: 3618-3625). This explains the differences between the concentrations used in vitro and in vivo.
Page 13, line 323: it is not necessary to say "...interesting study published during the preparation of this manuscript." This phrase should be deleted, and the relevant reference simply cited.
We will follow the reviewer’s recommendation.
The authors need to explain more clearly in the beginning what exactly is meant by "paradoxical" hyperactivity. They provide greater meaning later in the manuscript, but this should be clarified at the outset.
We will explain why we used this adjective in the beginning as recommended by the reviewer.
Reviewer #2 (Significance (Required)):
This is a very important study to show how primary defects in metabolism (i.e., disruption of the mitochondrial pyruvate carrier) can lead to epilepsy. Moreover, it details a primary mechanism that connects cellular bioenergetics to membrane excitability (through changes in calcium homeostasis and M-current function).
This is a well-conducted study that utilizes a multiplicity of experimental tools to link biochemistry with seizure activity. This type of study is not so readily done, and strengthens the notion that primary defects in metabolism can result in epileptic seizures.
This study is unique and attempts successfully to be more than just correlational. Hence it is a valuable contribution to the field.
The audience will likely consist of metabolic geneticists, neurologists/epileptologists, and neuroscientists. This is a beautiful study that runs the translational spectrum from biochemistry to behavior.
My expertise is in the field of translational epilepsy research, with a focus on mitochondria, metabolism, the ketogenic diet and ketone bodies. Thus, I am qualified to critically evaluate the entire manuscript.
**Referee Cross-commenting**
After reading comments and reviewing the manuscript again, would agree with Reviewer #1, and would change recommendation to MAJOR REVISION.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
This manuscript tests the genetic requirement of the mitochondrial pyruvate carrier (MPC) in regulation of neuronal excitability. The authors find that MPC deficiency in glutamatergic neurons is associated with aerobic glycolysis, inhibition of the M-type K channels, and neuronal hyperexcitability that manifests in increased sensitivity to chemical pro-convulsants without changes in resting conditions. Alterations in Ca homeostasis in MPC-deficient neurons is consistent with reduced mitochondrial membrane potential and attendant diminution of mitochondrial calcium buffering capacity. The authors further show that the effect of MPC deficiency can be phenocopied by treatment of wild type neurons with a chemical inhibitor of the mitochondrial Ca uniporter (MCU). Based on these data, it is proposed that reduced mitochondrial Ca uptake causes neuronal hyperexcitability in the absence of MPC. Overall, the manuscript presents detailed electrophysiology and in vivo seizure studies. However, there is significant disconnect between the actual data in Fig. 6 and the authors' conclusions/proposed mechanism. In particular, the evidence for the role of Ca in the hyperexcitability due to MPC deficiency is the weak link in the authors' argument.
- The studies linking reduced mitochondrial Ca uptake to hyperexcitability in MPC-deficient neurons (Fig. 6) have several limitations that significantly weaken the paper: 1a. The Ca measurements in cortical neurons (Fig. 6A-F) are performed under conditions (glutamate/KCl) that are fundamentally different from those used in electrophysiology of CA1 pyramidal neurons (Fig. 6G-N). The electrophysiological excitation is much briefer and less extreme than the chemical stimulation, and it is not clear that the Ca dysregulation occurs at the earliest times (see Fig. 6A).
This point was also raised by reviewer 1. Please see our response to point 2.
1b. The conclusion that MCU is functionally responsible for MPC's effect on neuronal excitability is singularly based on the use of RU360 as a chemical inhibitor of MCU but the specificity of this reagent is questionable. Evidence for a cause and effect relationship that directly implicates altered MCU/mitochondrial Ca buffering has not been provided.
This accurate point was also raised by the reviewer 1. Please see our response to point 2 for a complete response. We will downregulate expression of MCU using shRNAs. We will also measure the mitochondrial calcium level in the hope of better understanding whether the phenotype of the MPC-deficient mice is due to impaired mitochondrial calcium uptake.
1c. There is a large variation in the effect of 10 uM RU360 on firing frequency, comparing Fig. 6H and N (blue traces), including the shape of the traces and values at ramp number 6. This calls into question the reliability of the comparisons in each separate figure.
Data presented in each single graph in the main Figures were obtained from groups of littermates through recordings conducted in consecutive days. Some caution is warranted when comparing data between different figures (i.e. between different experimental series), as several factors may contribute to inter-experiment variability, including variability between different batches of animals. However, the difference pointed out by the reviewer regarding the values of cell firing reported in Fig. 6H and N is only apparent. When applying depolarizations with ramps of 5s, a fair amount of WT cells infused with RU-360 show high instantaneous firing frequency, especially for the last ramps that steeply reach high current levels. This leads to accommodation/inactivation of the action potential towards the end of the ramps, as shown in the example trace in Fig 6G. As a result, the current-frequency plot deviates from linearity, as it is the case in Fig 6H (blue trace) and, even more evidently, in Fig 6N. We have now reanalyzed the same recordings from WT cells infused with 10 µM RU-360 and measured the firing frequency in response to a square depolarizing step (250 pA) of 0.5 or 1 second. No difference was found between the firing frequencies of the cells from Fig 6H and Fig. 6N (group 1 and group 2, respectively, in the figure below). Although the ramps may lead to some distortion for higher stimulation levels, we have decided to show results from ramps consistently throughout the main figures because this protocol with continuously increasing currents allows us to measure more precisely the rheobase and the firing threshold (as opposed to the stepwise increments of a square stimulation).
1d. The calcium > PIP2 > M-type K+ channel axis is well established but has not been fully explored in the context of MPC deficiency. The use of a calcium chelator will likely be informative in this context, and would be better evidence for a role of Ca in the MPC effects.
Although the use of a Ca2+ chelator such as BAPTA is likely to introduce confounding effects through the inhibition of other Ca2+-dependent channels, we will try this option and assess whether a XE991-sensitive component will be unmasked in MPC deficient cells.
1e. The ability of BHB to rescue various parameters in this and other figures in the paper is interesting but does not directly speak to the specific mechanism as to how MPC deficiency affects neuronal excitability. BHB's effect is consistent with the metabolic flexibility of neurons when the TCA cycle cannot be fueled by glucose/pyruvate (as in GLUT1 or MPC deficiency).
The mechanism we propose to explain the hyperexcitability of MPC-deficient neurons relies on the low mitochondrial membrane potential and their decreased capacity to buffer calcium. Based on our data, we propose that calcium accumulation in the cytosol disrupts the CaM-KCNQ interaction leading to hyperexcitability. Indeed, BHB could act in two possible (and parallel) ways. 1: directly on the M-type channels, 2. on mitochondria by providing acetylCoA to the TCA cycle. The use of an alternative ketone body will be informative in disentangling these two possibilities.
The manuscript (and the field) will benefit from a more scholarly discussion and integration of published literature:
2a. The published studies on the outcome of pharmacologic MPC inhibition in neurons (Ref 18, Divakaruni et al.) are not only consistent with the bioenergetic effect in Fig. 1, but more importantly, show that interference with MPC does not lead to broad deficiencies in energy metabolism but rather remodel fuel utilization patterns to alternative substrates that feed the TCA cycle (BHB, leucine, etc). For this reason, terms such as "mitochondrial dysfunction" and "OXPHOS deficiency" used throughout the manuscript to describe MPC deficiency are vague and imprecise. In addition, this metabolic flexibility may explain lack of defects under resting conditions. In light of these considerations, the argument as to whether aerobic glycolysis in MPC-deficient neurons explains the lack of phenotype in resting conditions (p 17) seems one-sided. Overall, the studies in ref 18 are relevant to the current manuscript and should be better integrated in the discussion.
We fully agree with the possibility that the rewiring of cell metabolism in MPC-deficient neurons in the presence of leucine, BHB and other metabolites could explain the lack of phenotype in resting conditions. We thank the reviewer for this highly relevant comment which we will include in the revised discussion.
2b. Several references are cited to describe the role of OXPHOS vis-à-vis aerobic glycolysis in neuronal function. At times, however, the authors' statements are not consistent with what these papers actually show (or do not show). For example, see the use of refs 6 and 44 on p17 of the discussion, where the authors state that aerobic glycolysis uncoupled from OXPHOS is sufficient to provide ATP for normal neurotransmission, but this does not mean OXPHOS is not needed.
We agree that these references are not appropriate here and they will be removed.
2c. Although the XE991 experiments support an important role for the M-type channels in the altered excitability with deficiency, it is not clear that the proposed mechanism can explain all of the electrophysiological differences, particularly those resting properties that are measured without a Ca challenge to the neurons. It would be good to discuss other possible mechanisms that could affect neuronal excitability.
Our results point to M-type channels as important players in the phenotype of the MPC-deficient mice. Previous reports indicate that inhibition of this channel by XE991 can modulate input resistance, membrane potential and firing threshold of pyramidal cells (e.g. Shah et al, 2018, doi/10.1073/pnas.0802805105; Hu et al. 2007, DOI:10.1523/JNEUROSCI.4463-06.2007; Petrovic et al., 2012, doi:10.1371/journal.pone.0030402). We also found that XE991 induced a shift towards more negative potentials in the firing threshold of WT cells, but not in MPC1 deficient cells (-3.3±0.6 vs. -0.4±1.0, n=9, 8, p=0.027). However, we agree with the reviewer that the phenotype is probably highly complex and that additional mechanisms may contribute to modulate the intrinsic excitability of MPC-deficient neurons. One such mechanism could be closure of KATP channels, which we are currently investigating. This will be discussed.
Reviewer #3 (Significance (Required)):
The significance of the advance: The studies provide genetic evidence for the role of MPC in neuronal excitability.
The work in the context of existing literature: Please see specific comments above under point 2 regarding the need for a scholarly discussion and integration of existing literature.
Audience that might be interested: mitochondrial bioenergetics and metabolism and metabolic control of neuronal excitation.
Keywords describing expertise: metabolism, mitochondria and electrophysiology.
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Referee #3
Evidence, reproducibility and clarity
This manuscript tests the genetic requirement of the mitochondrial pyruvate carrier (MPC) in regulation of neuronal excitability. The authors find that MPC deficiency in glutamatergic neurons is associated with aerobic glycolysis, inhibition of the M-type K channels, and neuronal hyperexcitability that manifests in increased sensitivity to chemical pro-convulsants without changes in resting conditions. Alterations in Ca homeostasis in MPC-deficient neurons is consistent with reduced mitochondrial membrane potential and attendant diminution of mitochondrial calcium buffering capacity. The authors further show that the effect of MPC deficiency can be phenocopied by treatment of wild type neurons with a chemical inhibitor of the mitochondrial Ca uniporter (MCU). Based on these data, it is proposed that reduced mitochondrial Ca uptake causes neuronal hyperexcitability in the absence of MPC. Overall, the manuscript presents detailed electrophysiology and in vivo seizure studies. However, there is significant disconnect between the actual data in Fig. 6 and the authors' conclusions/proposed mechanism. In particular, the evidence for the role of Ca in the hyperexcitability due to MPC deficiency is the weak link in the authors' argument.
- The studies linking reduced mitochondrial Ca uptake to hyperexcitability in MPC-deficient neurons (Fig. 6) have several limitations that significantly weaken the paper:
1a. The Ca measurements in cortical neurons (Fig. 6A-F) are performed under conditions (glutamate/KCl) that are fundamentally different from those used in electrophysiology of CA1 pyramidal neurons (Fig. 6G-N). The electrophysiological excitation is much briefer and less extreme than the chemical stimulation, and it is not clear that the Ca dysregulation occurs at the earliest times (see Fig. 6A).
1b. The conclusion that MCU is functionally responsible for MPC's effect on neuronal excitability is singularly based on the use of RU360 as a chemical inhibitor of MCU but the specificity of this reagent is questionable. Evidence for a cause and effect relationship that directly implicates altered MCU/mitochondrial Ca buffering has not been provided.
1c. There is a large variation in the effect of 10 uM RU360 on firing frequency, comparing Fig. 6H and N (blue traces), including the shape of the traces and values at ramp number 6. This calls into question the reliability of the comparisons in each separate figure.
1d. The calcium > PIP2 > M-type K+ channel axis is well established but has not been fully explored in the context of MPC deficiency. The use of a calcium chelator will likely be informative in this context, and would be better evidence for a role of Ca in the MPC effects.
1e. The ability of BHB to rescue various parameters in this and other figures in the paper is interesting but does not directly speak to the specific mechanism as to how MPC deficiency affects neuronal excitability. BHB's effect is consistent with the metabolic flexibility of neurons when the TCA cycle cannot be fueled by glucose/pyruvate (as in GLUT1 or MPC deficiency).
- The manuscript (and the field) will benefit from a more scholarly discussion and integration of published literature:
2a. The published studies on the outcome of pharmacologic MPC inhibition in neurons (Ref 18, Divakaruni et al.) are not only consistent with the bioenergetic effect in Fig. 1, but more importantly, show that interference with MPC does not lead to broad deficiencies in energy metabolism but rather remodel fuel utilization patterns to alternative substrates that feed the TCA cycle (BHB, leucine, etc). For this reason, terms such as "mitochondrial dysfunction" and "OXPHOS deficiency" used throughout the manuscript to describe MPC deficiency are vague and imprecise. In addition, this metabolic flexibility may explain lack of defects under resting conditions. In light of these considerations, the argument as to whether aerobic glycolysis in MPC-deficient neurons explains the lack of phenotype in resting conditions (p 17) seems one-sided. Overall, the studies in ref 18 are relevant to the current manuscript and should be better integrated in the discussion.
2b. Several references are cited to describe the role of OXPHOS vis-à-vis aerobic glycolysis in neuronal function. At times, however, the authors' statements are not consistent with what these papers actually show (or do not show). For example, see the use of refs 6 and 44 on p17 of the discussion, where the authors state that aerobic glycolysis uncoupled from OXPHOS is sufficient to provide ATP for normal neurotransmission, but this does not mean OXPHOS is not needed.
2c. Although the XE991 experiments support an important role for the M-type channels in the altered excitability with deficiency, it is not clear that the proposed mechanism can explain all of the electrophysiological differences, particularly those resting properties that are measured without a Ca challenge to the neurons. It would be good to discuss other possible mechanisms that could affect neuronal excitability.
Significance
The significance of the advance: The studies provide genetic evidence for the role of MPC in neuronal excitability.
The work in the context of existing literature: Please see specific comments above under point 2 regarding the need for a scholarly discussion and integration of existing literature. Audience that might be interested: mitochondrial bioenergetics and metabolism and metabolic control of neuronal excitation.
Keywords describing expertise: metabolism, mitochondria and electrophysiology.
-
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Referee #2
Evidence, reproducibility and clarity
De la Rossa and colleagues examined the consequences of conditionally knocking out MPC1,a subunit of the mitochondrial pyruvate carrier. They found that despite decreased levels of oxidative phosphorylation in excitatory neurons, phenotypically these conditional knockout mice were normal at rest. However, when challenged by inhibition of GABA neurotransmission, these animals developed severe seizure activity and expired. These authors then showed that neurons with an absence of MPC1 were hyperexcitable in part through abnormal calcium homeostasis, which was associated with a reduction in M-type inhibitory potassium channel activity. Intriguingly, the ketogenic diet and the major ketone body beta-hydroxybutyrate were able to reverse these changes.
This is a carefully conducted research study that reveals cell type-specific alterations of MPC1 deletion and functional consequences. The study design was logical and involved an exhaustive array of methodologies. The manuscript was generally well written and organized, and there are no major concerns. This study shows a direct causal relationship between impaired bioenergetics at the level of mitochondrial, and subsequent behavioral seizures, and is perhaps the most direct demonstration to date that an intrinsic disturbance of metabolic function can result in seizure activity (through changes in calcium regulation and impairment of ion channel activity). This will be an important contribution to the scientific literature.
MINOR:
- Page 4, line 86: Would recommend changing "paroxystic" to "paroxysmal" (the latter which is a more recognized term).
- Page 5, line 124: recommend including the concentration of beta-hydroxybutyrate used when first mentioned. In general, concentration and dose information were difficult to find, as well as route of administration (for kainate, page 7, line 175). This type of information was not conveniently presented.
- Page 5, line 128: "both overcomed" is awkward. Would recommend using "both reversed".
- Page 8, line 193: the authors probably meant "astro-MPC1-WT mice", not "neuro-MPC1-WT mice".
- Page 12, lines 280-282: the authors might want to mention that chronic exposure of BHB might reduce the hyperexcitability of neuro-MPC1-KO mice.
- Please review entire manuscript and use consistent tense. For example, on page 13, line 309, to maintain the past tense, it should read "We first assessed whether..."
- Page 13, line 318: the authors used 10 mM BHB when examining calcium levels, but they earlier used 2 mM. They need to explain why they used a different concentration; and 2 vs 10 mM are quite different.
- Page 13, line 323: it is not necessary to say "...interesting study published during the preparation of this manuscript." This phrase should be deleted, and the relevant reference simply cited.
- The authors need to explain more clearly in the beginning what exactly is meant by "paradoxical" hyperactivity. They provide greater meaning later in the manuscript, but this should be clarified at the outset.
Significance
This is a very important study to show how primary defects in metabolism (i.e., disruption of the mitochondrial pyruvate carrier) can lead to epilepsy. Moreover, it details a primary mechanism that connects cellular bioenergetics to membrane excitability (through changes in calcium homeostasis and M-current function).
This is a well-conducted study that utilizes a multiplicity of experimental tools to link biochemistry with seizure activity. This type of study is not so readily done, and strengthens the notion that primary defects in metabolism can result in epileptic seizures.
This study is unique and attempts successfully to be more than just correlational. Hence it is a valuable contribution to the field.
The audience will likely consist of metabolic geneticists, neurologists/epileptologists, and neuroscientists. This is a beautiful study that runs the translational spectrum from biochemistry to behavior.
My expertise is in the field of translational epilepsy research, with a focus on mitochondria, metabolism, the ketogenic diet and ketone bodies. Thus, I am qualified to critically evaluate the entire manuscript.
Referee Cross-commenting
After reading comments and reviewing the manuscript again, would agree with Reviewer #1, and would change recommendation to MAJOR REVISION.
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Referee #1
Evidence, reproducibility and clarity
The authors have presented a very interesting and compelling set of data regarding the impact of conditional deletion of the only known pathway allowing the uptake of pyruvate into mitochondria. The paper comprises two interwoven stories that are both important. The first is the remarkable finding that the majority of excitatory neurons in the cortex (i.e. those under the influence of the CaMKII promoter)show remarkable metabolic flexibility as they tolerate elimination of pyruvate oxidation, considered the major supplier of ATP in neurons. The data on this seem clear although the authors did not delve into the potential mechanisms of metabolic compensation that likely occurs. Instead they examined whether there was some mal-adaptive compensation and they found clear evidence of this: in the absence of MPC activity the mice are much more prone to epileptic seizures, unveiled experimentally by relatively standard protocols (kindling). The authors present largely very convincing evidence that this mal-adaptive compensation in turn ends up decreasing the activity of KV7.2/7.3 channels whose job is normally to limit runaway repetitive firing by mediating an hyperpolarizing K+ efflux following an action potential. This channel, put on the map as it was one of the downstream targets modulated by cholinergic metabotropic activation, is also know known to be controlled by Calmodulin and therefore cytosolic Ca levels. Overall, I think at its core this manuscript is interesting and important. There however several weaknesses, I fear, will diminish the impact on the eventual readership. If these points can be addressed, it will strengthen the longevity of these findings:
1) It is puzzling why the authors resorted to using shRNA-mediated KD of MPC1 for some of the in vitro studies when they have gone to the trouble of making a floxed CRE-dependent mouse. Primary cells (e.g. Fig 1) or organotypic cultures (Fig. 6) from these mice would have made a more consistent set of starting conditions to compare data across the manuscript. As there viruses expressing the CRE recombinase are widely available this could have been used on mice simply harboring the floxed gene it they are worried about waiting for the expression of the CaMKII promoter for in-vitro conditions.
2) The data in Figure 5 gets a little less convincing as using extracellular glutamate to drive Ca elevations is so non-physiological that the results might really be distorted by the participation of something irrelevant to the story, even though it supports the overall interpretation for a role of Ca/CaM in the control of the channel. Similarly, the use of RU360 should be done with caution. The drug, although a useful antagonist of MCU in purified mitochondria, is famously finicky with respect to its ability to cross membranes and could well have off target impact. A much cleaner experiment would be to suppress the expression of MCU via KD. Presumably in the MPC-deficient neurons, this would have minimal impact on Ca signals. Given the frequent ambiguity associated with interpreting pharmacological results, coupled to the central importance of this finding in interpreting the entire paper, I think carrying out experiments with molecular genetic manipulation of MCU is warranted.
3) The authors have not really made clear in this paper whether the ability to suppress the phenotype of the MPC deficiency with ketones is really related to a providing TCA cycle support or instead a pharmacological impact on non-TCA related targets (such as the Kv7.2/7.3 channels). Presumably the use of other ketones might circumvent this. The action of ketone bodies has been a topic of considerable interest in neuroscience, given the clinical relevance for childhood epilepsies. Previous studies for example have argued for direct inhibition of the vesicular glutamate transporter (Juge et al. Neuron 2010). The use of other ketones (acetoacetate) would narrow down the interpretations of the data.
other
1) In vitro - scramble controls only serve to demonstrate there is no general effect of treating cells with shRNAs, but do not address if there is an off-target effect. The most convincing thing here would be to have an shRNA-insensitive variant that rescues.
2) Does rescuing CaMK binding to KCNQ channels rescue the phenotypes?
3) As the authors imply that BHB activates KCNQ channels, showing this directly in their prep would provide some convincing data. If this is true, why doesn't BHB increase firing rate of WT neurons?
4) How does the anti-epileptic effects of ketones in this study relate to previous reports of regulation of KATP channels? One of main concerns is that ketones might have a parallel anti-epileptic effect in the MPC1 KO mice that is unrelated to the mechanism proposed here.
Minor comments:
1- What is the MPC1 KO efficiency in CaMK neurons? The western blot in 2c is from the whole cortex and therefore does not show that. 2- Mitochondrial Ca2+ levels are not measured directly, for which there are many tools. This is needed to demonstrate definitively that there is a defect in Ca2+ handling."
Significance
see above.
Referee Cross-commenting
It seems we are in reasonable agreement about the pros & cons of the manuscript. I agree that alternative approaches to RU360 are warranted.
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Referee #1
Evidence, reproducibility and clarity
This study seeks to define how human lysosomes selectively downregulate membrane proteins and identify the machinery involved in this process. To this end, the authors screened a set of 30 lysosome membrane proteins (LMPs) in a cycloheximide chase assay in a human cell line which led to the identification of RNF152 (an E3 ligase) as a particularly short lived LMP. Further experiments demonstrate that RNF152 degradation is ubiquitin, ESCRT and lysosome dependent. They also show that the E3 ubiquitin ligase activity of RNF152 is critical for its turnover. The overall technical quality of the experiments is high and conclusions about the degradation of RNF152 are mostly reasonable. My most significant concern is that while compelling data is provided for RNF152 turnover, the authors over-reach in their efforts to generalize their findings to other LMPs. Given that the E3 ligase activity of RNF152 is so important for its turnover, RNF152 might be a special case. Consistent with this, the authors did not characterize other LMPs with similarly high rates of turnover. Although it would be interesting if RNF152 regulates the stability of other LMPs, until such proteins are identified, the authors should be more cautious in their interpretation. Speculation on this matter is reasonable so long as it is labeled as such. Even with respect to RNF152 turnover mechanisms, the overall conclusions would be significantly strengthened by a demonstration that the endogenously expressed, untagged protein behaves in a similar manner to what was described for the GFP-tagged transgene. With respect to the question about how long it would take for the authors to address these concerns, I cannot give a precise answer as it would depend on whether they decide to much more narrowly interpret their findings and temper their major claims (less than a month) or to expand efforts to generalize results (time frame unknown and perhaps not feasible).
- As a specific (but not the only) example of over-reaching in generalizing the findings, the abstract ends with the following statement: "Thus, our study uncovered a conserved mechanism to down-regulate lysosome membrane proteins." My concern is that although this mechanism might be generalizable, the authors have only presented data for RNF152.
- There is a complete reliance on over-expressed, GFP-tagged RNF152. There is no demonstration that the endogenously expressed protein undergoes such high rates of turnover. It is thus possible that the data does not reflect the normal turnover pathway for this protein.
- In Figure 2B, why is the loss of full length RNF152-GFP not accompanied by an increase in the signal for free GFP during these pulse-chase experiments?
- Figure 2E: Were all of the pairs of Input and IP immunoblots subject to the same exposure and image adjustments?
- Figure 3C-E: The RNF152 mutants have slowed but not eliminated degradation. Is this dependent on their association with or ubiquitination by the endogenouslyh expressed RNF152?
- Methods section indicates that t-tests were performed for all statistics. However, many experiments contain multiple comparisons and are thus ideally suited to t-tests. The authors should either justify the use of t-tests or provide a more suitable statistical analysis.
- Although the model in Figure 7 shows the E3 (RNF152) ubiquitinating other proteins and promoting their ESCRT-dependent sorting into ILVs, this study did not identifying any such clients of RNF152.
Minor
Page 3: "Without treatment, almost all types of LSD patients will develop severe neurodegeneration in the central nervous system." This statement is misleading as there are multiple forms of LSDs that do not result in neurodegeneration and it is only these LSDs which can be successfully treated via enzyme replacement therapies. Unfortunately, the neuropathic LSDs remain largely untreatable due largely to issues of blood brain barrier permeability.
Page 3: "As we age, the lysosome membrane gradually accumulates damaged proteins and loses its activity, which dampens the cell's ability to remove pathogenic protein aggregates and damaged organelles, eventually leading to cell death and inflammation (Carmona-Gutierrez et al., 2016; Cheon et al., 2019; Yambire et al., 2019)." The references provided do not provide sufficient direct support for this broad statement.
Page 10: STED imaging results (currently "data not shown") should be supported by showing the relevant data.
Camera and objective information should be provided for microscopy studies.
Significance
The identification of a generalizable mechanism for the turnover of mammalian LMPs would represent a significant advance and would raise many interesting questions about mechanisms, regulations and physiological impact. While this studies contributes some interesting new clues to this topic, it falls short of unambiguously establishing how most LMPs are turned over in human cells. The data with respect to RNF152 is intriguing as it supports the idea that a novel form of ESCRT-dependent protein clearance occurs at the limiting membrane of lysosomes. However, it remains very much unclear to what extent this can be generalized to other proteins.
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Referee #2
Evidence, reproducibility and clarity
The mechanisms involved in lysosome membrane protein turnover are not well understood. Weichao et al. used a cycloheximide chase screen and overexpression 30+ lysosome membrane proteins in HEK293 cells to identify LMPs (lysosome membrane proteins) with fast turnover rates. They identified RNF152 as a suitable candidate for study given its high turnover rate and physiological relevance. They showed that RNF152's levels were regulated by ubiquitination by mutating cytosolic lysine residues and RNF152's ring domain and finding that these changes increased RNF152 stability. The researchers found that knocking down ESCRTIII and overexpressing a dominant-negative mutant of VPS4 increased RNF152 levels at steady-state and delayed RNF152 turnover. When expressed in yeast, RNF152 is localized on vacuole membrane and is also subject to regulation by the ESCRT pathway. Early ESCRT pathway members are essential for RNF152 degradation in yeast but not in mammalian cells. Taken together, these findings are important for furthering our understanding of how the levels of lysosome membrane proteins are regulated. A better understanding of ESCRT mediated LMP degradation is important not only for understanding mechanisms involved in controlling lysosomal activities but also for therapeutic development for many diseases involving dysregulation of LMP protein levels.
However, the following concerns should be addressed before the paper is published:
- The authors have found that among 30 LMPs, three LMPs, LAPTM4A, RNF152, and OCA2, have half-lives less than 9 hours. RNF152 is a ubiquitin ligase and the authors showed that auto-ubiquitination is important for the recognition by the ESCRT machinery. Can the authors speculate how the ligase activity of RNF152 is regulated? Also, is similar mechanism involved in LAPTM4A and OCA2 turnover? Are these two proteins also ubiquitinated?
- The authors should at least demonstrate that endogenous RNF152 levels and turnover are also regulated by ESCRT III and VPS4, using the stable cell lines the authors have already made. All of the mammalian cell experiments are performed using overexpression of RNF152, and an endogenous experiment would inspire confidence that the author's findings are not an artifact of over-expression.
- While the authors showed that the K->R and C->S mutants of RNF152 have increased stability, it would be more compelling if they could perform an IP using HA-ubiquitin to prove this effect is due to a loss/reduction of RNF152 ubiquitination and not due to other changes in the protein. Another concern is whether mutating 8 lysine or 4 cysteine residues simultaneously would affect the folding of the protein, leading to abnormal aggregation in the cell.
- For some of the data, statistical analysis is missing: a. All of the cycloheximide chase experiments. b. statistical significance for the puncta vs membrane GFP signal data shown in figure 6f c. The flow cytometry data
- Fig. 4A and Fig. S2A, why MG132 treatment affects the levels of free GFP if it's inside of the lysosome?
- Make sure that the figures are properly referenced in the text, there is one instance where the authors referenced figure 2d, when they clearly meant to reference figure 2e, and figure 2e where the authors meant to reference figure 2f etc.
Minor Comments:
- In figure 1A, at CHX 3h, there's ~40% reduction of GFP-RNF152, however, in the rest of the figures, such as figure 2B,at CHX 2h, there's ~70-80% reduction of GFP-RNF152. How to explain the difference in the kinetics?
- In figure 2F, it is hard to differentiate when the underline for input ends and the underline for IP begins unless the reader zooms in, please separate them a bit more.
- Fig. 4F, it's very hard to see the red and green signals, maybe get rid of the DAPI channel increase the intensity for both green and red channels, and zoom in?
- Scale bars are missing in the insert images in figure 1C, figure 4G and figure 6E.
- In figure S1, the labels do not match with the blot for GFP-TMEM106B time points.
Significance
These findings are important for furthering our understanding of how the levels of lysosome membrane proteins are regulated. A better understanding of ESCRT mediated LMP degradation is important not only for understanding mechanisms involved in controlling lysosomal activities but also for therapeutic development for many diseases involving dysregulation of LMP protein levels.
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Referee #3
Evidence, reproducibility and clarity
Summary
Lysosomes play key roles in cellular homeostasis by functioning as a signaling hub for growth control and acting as a terminal catabolic station. Deregulation of lysosomes are now linked to multiple human diseases including cancer, neurodegeneration and etc. An emerging topic of interests in lysosomal biology is the regulation of lysosomal proteostasis and how it impacts the overall fitness and functionality of the lysosome per se. Zhang et al presents here a case study of quality control of lysosomal membrane proteins, with a focus on the turnover of a lysosomal anchor E3 ubiquitin ligase RNF152. They showed that RNF152 is rapidly degraded through an ESCRT-dependent fashion and that this mechanism is also conserved in yeast.
Major comments:
- The writing of the manuscript including the abstract could be further polished. The manuscript in its present form appears to be a technical report that does not sufficiently convey the significance of this study.
- Cyclohexamide is commonly used in studying the half-lives of proteins of interests. This is not a new method authors developed in the first place.
- The data of protein turnover was presented by plotting the relative level of proteins as a function of time. But the use of degradation kinetics was all over the place in the manuscript, which is inappropriate scientifically. The authors should first generate fit to first order decay to acquire a degradation rate constant, k (min-1) and calculate half-life (T1/2) from there.
- What are the functional consequences of RNF152 degradation? What are the biological impacts at both lysosomal and cellular levels in RNF152-depleted cells?
- Given the rapid turnover of RNF152 at basal state, one can predict that this protein may become functionally important under specific circumstances, for example, certain stress. This aspect is worth exploring.
- The authors chose RNF152 over OCA2, a melanosome-specific protein. However, OCA2 was shown to colocalize with LAMP2 much better than RNF152.
Minor comments:
- Mislabeling and typo errors detected in the text: a. Page 7 "As expected, the full-length GFP-RNF152 and other lysosomal proteins such as LAMP2 and cathepsin D (CTSD) were enriched by Lyso-IP. In contrast, PDI (ER), Golgin160 (Golgi), EEA1 (endosomes), and GAPDH (cytosol) were not enriched (Figure 2D)." - should be Figure 2E instead. b. Page 7 "Our result confirmed that the lysosome population of GFP-RNF152 is quickly turned over, while LAMP2 is very stable on the lysosome (Figure 2E)." - should be Figure 2F instead. c. Page 14 "knocking down either TSG101 or both TSG101 and RNF152 only had a minor impact on the degradation kinetics of GFP-RNF152 (Figure S3A-B)." - should be ALIX instead of RNF152.
- Stable cells expressing GFP-RNF152 or 3xFLAG-RNF152 were primarily used in this study. It will be useful to perform some experiments by examining the endogenous counterpart using antibodies against RNF152. For example, Figure 2D and 2E.
- For all the flow cytometry analysis, the value of GFP intensity in respective graphs should be indicated.
- Statistics analysis was not performed on Figure 5D.
- In Figure 6D and J, what are the reasons for the appearance of multiple peaks, particularly, by the red line?
- In Figure 3A, the question marks should be removed to avoid confusion. "Predicted" can be used instead if there is no direct evidence from mass spec analysis.
- In Figure 3C, the authors identified two mutants including KR and CS that are refractory to degradation. It will be more insightful by showing the ubiquitination of these two mutants as in Figure 3B.
Significance
Multiple mechanisms including ESCRT complex have been reported to regulate the quality control of lysosomes. Understanding the roles of each mechanisms and selection of their substrates in maintenance of lysosomal integrity is of great interest in cell biology. Zhang and colleagues showed a case study of RNF152, a substrate of ESCRT-dependent degradation, but did not further pursue the biological functions of RNF152. This somewhat limits the conceptual advance of the study.
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Reply to the reviewers
The authors do not wish to provide a response at this time.
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Reply to the reviewers
We would like to thank the editor for their consideration and the reviewers for their time and thoughtful comments. Below we have written a point-by-point response to their comments and concerns. The original comments are displayed in italic fonts, whereas our responses are in regular fonts for clarity.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
The submitted manuscript 'Identification of phenotype-specific networks from paired gene expression-cell shape imaging data' of Barker et al. uses a convolute of different bioinformatics tools (see Key Resource Table) to analyze reported RNA sequencing data and to correlate derived pathways with imaging features of breast cancer cell lines based on specific pathway constructions. The thin red line of the data presentation in the manuscript is not obvious.
\*Major concerns:***
1.1 The main biological 'finding' of the study RAP1 'as a potential mediator between the sensing of mechanical stimuli and regulation of NFkB activity' is reported and therefore the assumption 'how exactly extra-cellular mechanical cues are sensed by the cell and passed on to NFkB in breast cancer is not understood' is misleading. Please review: https://www.nature.com/articles/ncb2080** (human breast cancers with NF-κB hyperactivity show elevated levels of cytoplasmic Rap1. Similar to inhibiting NF-κB, knockdown of Rap1 sensitizes breast cancer cells to apoptosis) https://pubmed.ncbi.nlm.nih.gov/17510404**/ (RAP1 is a crucial element in organizing acinar structure and inducing lumen formation), and https://pubmed.ncbi.nlm.nih.gov/21429211/**.
R1.1 We thank the reviewer for pointing out these references. Teo et al. (which is cited in our manuscript) provides evidence that Rap1 regulates IKK and therefore NFkB in breast cancer, while Itoh et al. and McSherry et al. focus on Rap1’s ability to modulate migration and morphogenesis as do other similar papers cited in our manuscript. None of the papers show the significance of the Rap1-NFkB interaction in the explicit context of cell shape with Teo et al. only speculatively mentioning a potential relevance of Rap1/NFkB in migration (“Given that NF-κB is critical for [. . . ] stimulating invasion, our results document a clinical setting wherein Rap1-mediated regulation of NF-κB could be critical.”). We appreciate that the specific sentence the reviewer has drawn attention to is slightly misleading given Teo et al. and we will amend it in the revised manuscript. However, here, we use a novel methodology on a past dataset to link the concepts introduced by these 3 papers within the specific context of cellular morphology in breast cancer cells.
Specifically, in this manuscript, we identify a Rap1 expression module correlated with cell shape and find that it is at the network confluence of transcription factors activated by cell shape. This, along with our findings of modulation of NFkB co-activators, as well as previous work showing that it is a key mechano-transductive transcription factor leads us to hypothesize that Rap1 mediates the regulation and mechano-sensing of cell shape via its interaction with NFkB.
It is also important to note that, while we build on the findings of Teo et al., McSherry et al. and Itoh et al. relating NFkB, Rap1 and cell shape, we also use our method to focus on other proteins of interest. These are drawn attention to in the discussion, with the ARNT KO/TNFalpha module being the most highly correlated gene expression module with the morphological features. Also, the importance of transcriptional co-regulators of NFkB are illustrated in the network propagation, with both NR0B2 and PPARGC1A mentioned in the discussion. However, our analysis naturally concentrates on the node with the most apparent literature support, which as your reading suggests is Rap1. The significance of this manuscript is that it is an unbiased systems-based methodology used to link cell-shape with signaling, via transcription in a context-specific manner (i.e. in the context of breast cancer). This produces a phenotype-specific network that has allowed us to connect diverse mechanisms and hypotheses put forward by other authors and further our understanding of how signaling manages the sensing and regulation of cell shape in breast cancer. The methodology is also applicable to any paired transcriptomics/phenotype dataset.
1.2 Besides, Fig. 2 and 3 are unrelated to this main statements.
R1.2 Figure 2 shows the results of our morphological cluster identification and subsequent differential expression analysis. Since these were included as parts of the network, we included them to give the reader an idea of the components included by this step. Figure 3A shows the network that was generated by our pipeline which forms the basis of all subsequent biological exploration, and the discovery of Rap1 and nodes important for the regulation of cell shape. Figure 3B shows that no bias was introduced by using the specific algorithm for our network generation. As such Figures 2 and 3 are related to the generation of the cell shape-specific network that forms the basis of our study. We will amend the text and figure legends to clarify this point more carefully, and we will consider moving some of the panels to the supplementary materials to simplify the message.
1.3. The spotted RAP1 (by TFs JARD2 and RUNX2) finding is not obvious without Fig. 4 results, a network propagation of functional TFs in differentially activated processes (basal vs. luminal) in the cell shape regulatory network. Please show that RAP1 could be not identified without the network based on TF and DEG only.
R1.3 The Rap1 hypothesis is supported by both Figure S2E and Figure 4. Figure S2E shows that the Rap1 pathway-enriched gene expression module is the most differentially expressed module among those incorporated in our cell shape regulatory network. This suggests that this module is correlated to cell shape on a transcriptomic level, but does not necessarily mean anything within the context of intracellular signaling. Figure 4 shows that this gene expression module is at the confluence of activated transcription factors as specified by our constructed signaling network. This is an interesting finding as it implies (unlike Figure S2E) that the Rap1 gene expression module is relevant to intra-cellular signaling.
While the Rap1 module is indeed differentially expressed and could in theory have been found just by the DE analysis as being important, the network approach enables us to integrate these modules of co-expressed genes within known signaling networks. This allows us to go further than just making comments about expression and transcription factor activity, to discussing how signaling networks interact with our identified gene expression modules. This in turn allows us to construct more sophisticated hypotheses about cell shape regulation.
Particularly, we use this analysis to reinforce the association with Rap1 by illustrating that the Rap1 network node lies at the confluence of transcription factors activated in luminal-like and basal-like cell shapes. We also use the network to identify highly central nodes (such as PPARGC1A, CTNNB1 and ESR1) and other proteins identified in the network propagation (YAP1, IKBKB and ARNT). Furthermore, the network is used as a means of integrating gene expression modules in their signaling network environment. The method by which this embedding was done (in-going edges being transcription factors regulating the module and out-going edges being signaling proteins contained within the module) adds context specificity to a network that is otherwise generalised to many cell-types and contexts.
The lack of clarity on how we arrived at Rap1 as a key tenet of our discussion, as well as the added value to the methodology of the network analysis is something that we will certainly work on in our revision and we thank the reviewer for their valuable feedback. We will also move Figure S2E from the supplementary figures to the main Figure panels, as it is an important part of how we arrived upon Rap1 as a module of particular interest.
1.4 More complex fluorescence phenotypes are available and do not match the complexity of the RNASeq data, data input and pathway construction with only 10 simple cell shape features. Conversely, relative 'monoclonal' breast cancer cell lines may are the only application for this workflow.
R1.4 We thank the reviewer for their comment and respectfully disagree. These cell shape features were sufficient for the original authors Sero et al. to predict TF activities (PMID: 26148352) and Sailem et al. to identify clinically predictive metagenes (PMID: 27864353). Although these features seem simplistic, they concisely summarise a highly complex phenotype and are proven to encode metastatic potential (PMCID: PMC6976289) and to be prognostic markers for breast cancer progression (PMID: 28977854). Accordingly, these features are re-analysed using our workflow to better understand the signaling that drives them. Understanding other features that might match the complexity of our expression data is possible using the presented method, but is outside of the scope of the research within this manuscript as our research question focuses on the regulation of cell shape in breast cancer.
As evidence that this cell shape network is applicable beyond cell lines, we can perform an analysis on breast cancer patient data from the TCGA, demonstrating the relationship of our network’s components with metastasis, which is highly related to cell shape.
1.5 Image features Fig. 1 and 5 do not match
R1.5 It is true that the features in Fig.1 and Fig.5 do not exactly match. This is because these two datasets came from different studies. While they are slightly different features, the essential phenotypes that they quantify are the same. For example, in Fig 5., cytoplasm area, cytoplasm perimeter, nucleus area, nucleus length, nucleus width and nucleus perimeter, are clearly basic morphological features that are analogous to features in Fig.1, such as cell area, cell width to length, nucleus area, nucleus width to length. It is a solid assumption that the biological processes that drive these features are common, and our results illustrate this. Meanwhile, the existence of features measured in the dataset in Fig.5, that are not analogous to those used in the dataset used for model construction, provide convenient negative controls in order to determine that our network describes regulatory processes specific to the features used in network construction.
1.6 with Fig. 5 being a rather indirect 'proof' of usability.
R1.6 The purpose of Figure 5 is not to demonstrate usability but to prove that the network that we have identified is indeed representing cell signalling that controls cell shape. It shows that perturbations inside our network have a significantly stronger effect on phenotypes used in the creation of the network than perturbations outside our network. Moreover, it shows that this is not the case for phenotype features not used in the creation of our network, underlining that our network is both accurate and specific to the phenotypes used as input. We will add further clarifications in the text and figure legend to explain this better.
1.7 Fig. 1a has not achieved a visual descriptive state and asking a lot.
R1.7 We apologize for the lack of clarity here and will revise the figure to better present the method and reduce confusion.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
The authors combine single cell morphology and gene expression data to identify signaling activities implicated in the control of cellular morphogenesis. They describe a reasonable bioinformatics pipeline from gene expression shifts between two morphological phenotypes to pathways, then to common transcription factors to signaling. As far as I can assess the situation (I am not familiar with all the tools they use) the proposed pipeline works convincingly.
We would like to thank their reviewer for their thoughtful comments and to clarify that the analysis has not been done on single cell gene expression data, but rather on bulk RNAseq data. This is further explained in the point-by-point responses below.
2.1 However, I am concerned that the logic underlying this analysis is only partially valid. The link between signaling and morphology may be more direct than via TF-based gene expression regulation. Many signals (and many of the kinases the authors test for validation) are implicated in morphology control as direct upstream regulators of cytoskeleton dynamics and adhesion. This also applies to the GTPase Rap1, which the authors fish out as the most differentially expressed signal between two types of morphologies. In addition to the indirect effect of Rap1 on morphology via NFKB regulation suggested by the authors, Rap1 will affect morphology probably very directly through activation of Rac -> F-actin and RIAM -> nascent adhesions. At minimum, the authors should discuss this complexity as a caveat of their approach. And dependent on the impact the authors hope to have with this story, I believe they should experimentally resolve the ambiguity of direct vs indirect signaling for some of their key interpretations.
R2.1 We thank the reviewer for making this fair point about the limitations of our data, i.e that we are not able to directly observe and delineate exactly how upstream signaling has modulated or is modulated by cell shape. As a first major clarification, which we will make sure to include in the text, the Rap1 node doesn’t necessarily represent the Rap1 GTPase itself. It is a co-expression module that is enriched in activators and downstream effectors of Rap1 signalling. As such when we are talking about the Rap1 module we mean the subnetwork of Rap1 signalling rather than the specific small GTPase itself. Thus, we can’t assume that Rap1 itself is the key node in this subnetwork and it is therefore complicated to design specific experiments to test the direct or indirect modulation of cell shape by Rap1. We agree however that additional information regarding the role of this module in regulating cell shape would be interesting and valuable.
For this study, we have access to transcriptomic and cell shape data from 14 cell lines with transcriptomic and cell shape data. Using the expression data, we will quantify Rap1 expression module activity and its relationship to NFkB transcriptional activity across these cell lines. By comparing in these cell lines the effect on morphology when NFkB and the Rap1 module are combinatorially activated or deactivated, we can disseminate between competing hypotheses for direct and indirect activities of these two factors on cell shape. For example, if the overwhelming source of Rap1 module’s function was via direct interaction with F-actin, then Rap1 module activity would be predictive of cell shape, regardless of NFkB activation. A caveat to this is our limited access to only 14 cell lines. Additionally, if necessary, we have access to drugs that can induce cytoskeletal defects and perturb morphology directly. This can be used to disrupt the relationship between Rap1 and F-actin that the reviewer has identified and gauge the effect on cell shape. If such an intervention disrupts the relationship between Rap1 signaling module/NFkB transcriptional activity and cell shape then we can hypothesise that the activity of Rap1 signaling is greater than just its direct activity on F-actin. Finally, we can perform a knock-down of Rap1 (or selected components of its module) and NFkB itself and gauge the effect of such a perturbation on the Rap1 gene expression module and cell shape.
That being said, these signaling modulations (whether indirect or direct) are reflected accordingly in differentially activated transcription factors, and therefore can be observed and recorded from expression data. This is an interesting finding, as it implies that signaling processes not explicitly making use of transcription factors (such as those that directly affect adhesion complexes, regulating cytoskeletal proteins etc) can still have their activity gauged through their indirect downstream expression signatures. In any case, our findings illustrate that there is a cell shape-specific modulation of the Rap1 module in breast cancer, reflected in the expression data. Rap1 almost certainly has some direct contributions to cytoskeletal dynamics in breast cancer (PMID: 10805781, PMID: 30156466 and PMID: 22644079), but here we observe clearly how it also is modulating transcription factors, that we hypothesise may contribute to the development of a morphological and transcriptomic ‘niche’ in a more robust and long-term fashion. Nonetheless, the points discussed by the reviewer are valuable and in our revision we will discuss this as a potential caveat.
In defense to the presented premise, the authors start out by looking for correlation between gene expression and morphology, and they find some signal. Correlation analysis, especially in large data sets, tends to be pretty robust and specific, even on presence of strong confounders. Thus, even though the correlation expression-morphology, which points indirectly at morphology-regulating signaling modules, is likely to be super-imposed by direct morphology-regulating signaling pathways the proposed approach will not be able to detect, the presented analysis is valuable, in principle.
We thank the reviewer for their positive comments.
That said, I have a number of substantial concerns also with the implementation and presentation of the approach.
2.2 First, on the presentation side, for a paper that talks about cell morphology it is strange to have not a single figure panel showing an image of cells, or at least cell outlines. As a reader I would like to get visual impression of how different a high vs low Rap1 gene expresser is, for example.
R2.2 - We agree that it would greatly help the clarity and message of the manuscript. As we are not able to use the public and previously published data that have been used for our paper due to copyright laws associated with journal publications, we will generate relevant images representative of the respective cell shapes and include them in the manuscript.
2.3 Along the same lines, it is not quite clear to me when the authors collate entire cell lines into a single phenotype, do they switch then to population-based analysis? That is, for example the volcano plots in 2B,C are they representing an average gene expression shift?
R2.3 - We apologise for the lack of clarity. The morphological clustering and differential expression illustrated in Figure 2 is to find expression signatures responsible for distinct breast cancer cell shapes. We link our expression data and our imaging data via the breast cancer cell lines and so are limited to studying expression in bulk per cell lines. The volcano plots in 2B,C are of the differentially expressed genes (as calculated by DESEQ2) in morphologically distinct clusters of cell lines as specified by Figure 2A. This was collated so we could observe transcriptomic differences accounting for cellular morphology, rather than differences in cell lines (these being already well characterised and not in the scope of this manuscript).
We will add additional clarifications in our revised manuscript to further explain this.
2.4 How heterogeneous are the morphological signals?
R2.4 We provide values of standard deviation for the morphological features of the derived clusters (page 4 - “Clustering based on morphology reveals distinctive cell-line shapes”). The heterogeneity of the morphological clusters is minimised as per the elbow plot shown in Figure S2A. This plot illustrates the decreasing total within-cluster variation of the cell shape groups as the number of clusters (k) is increased. The point of inflection represents the optimum number of clusters (in our case k=3). Aside from this, we note that one of those 3 clusters is significantly more heterogeneous both morphologically speaking and biologically speaking (illustrated Figure 2A) and so we used the other two which showed more informative gene expression profiles and could be annotated roughly with breast cancer subtypes (basal and luminal - although is alignment was not perfect since the grouping was based only on the morphology). We took the more heterogeneous cluster (cluster A, Figure 2A) to be the least relevant cluster in terms of morphology and biologically significance, also because it contained the non-tumorigenic cell-line MCF10A.
2.5 Are the correlations between gene expression and morphology computed with single cell data as the basis?
R2.5 Due to the availability only of bulk RNA sequencing data for the cell lines for which we also had high content imaging data, all analyses are done using bulk RNA sequencing data at the cell line level. We will clarify this in the text and methods section.
2.6 Could the volcano plots be sharpened by accounting for the single cell variation in morphology instead of lumping the cells into two morphological classes?
R2.6 As per the limitations mentioned in R2.3 and R2.5, we cannot study gene expression at the single cell level. Furthermore, the utility of using morphological clusters was so that we could observe morphological transcriptomic traits rather than those specific to cell lines.
2.7 On the back end of the paper, when the authors apply kinase inhibitors to validate some of the claimed pathways, it would be nice for the reader to see the morphological effects of these inhibitors. And to relate the kinase induced shifts to the morphological heterogeneity that is the basis for the study driving, initial correlation analysis? At the end of the day, the proof is in the pudding.
R2.7 - We thank the reviewer for his very good point, and it would certainly improve the manuscript. We will attempt to source a visual illustration of the effect of kinase inhibitors on the breast cancer cells. However, the dataset we source this data from is publicly available, but unpublished and so our use is constrained by the terms of use of LINCs. We will contact the LINCS consortium to acquire permission and if they allow, we will certainly include them in our revised manuscript.
2.8 Finally, cell morphology regulation is a pretty foundational process of life. One therefore wonders whether the pathways the authors pulled out of their analysis work also in other cell types, beyond breast cancer cells? What if they pooled data from different cell types that cover the morphological state space more broadly?
R2.8 We thank the reviewer for this interesting point. We have observed that many if not most of the general processes identified, i.e. developmental pathways, extracellular matrix regulatory pathways and adhesion pathways, are already known to be associated with cell shape regulation and mechanotransduction in many different cell types. Thus, at the ‘big picture’ level, our findings hold across multiple cell types. However, the precise wiring of our network seems to be breast cancer specific. This is evidenced by the fact that when we try to use the LINCS data from other cell types to see if our network still holds in these contexts, we do not observe significant increase in changes in morphology when perturbing central nodes within our network compared to outside of our network. This is not unexpected: depending on the individual molecular background of each tissue and tumour type, signalling networks are known to be wired differently. Indeed, our method that uses the context- and cell feature- specific gene expression modules and the transcription factors that regulate them as a basis for extracting our cell shape signalling network allow for identification of exactly its specific wiring in the context used for training, i.e. the breast cancer cells. It would be very interesting to repeat our analysis on similar data on a different tissue type to identify parts of the network that seem to be identical versus those that differ. We have not been able yet to identify public systematic high content imaging data for a different tissue across multiple cell lines, but we will continue to look for such a dataset in the literature and through our network of collaborators. We will also explore the possibility of extracting such information from images from the TCGA to perform this analysis across patients of a specific cancer type, although admittedly we are not sure how feasible it would be to extract analogous features as the ones used for the breast cancer network from the images available. We will also add this point to the discussion.
Reviewer #2 (Significance):
The premise of this manuscript is very exciting and interesting: Is it possible to identify from a correlation of cell morphology and single cell gene expression the underlying cell signaling states that control morphology? Answers to this will begin to shed some light on the black box relation of morphology as an informant of cell states, which has been exploited by pathologists, physiologists, and cell biologists for more than a century, and which has seen a sharp revival recently thanks to deep learning, which is exceedingly good at finding correlations between data patterns.
This paper would have a broad audience in quantitative cell biology, systems biology, and perhaps also life data science and cancer (although the cancer aspect is marginal).
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
\*Summary***
In this work Barker et al. used computational approaches to analyze several existing data sets (including morphology and expression) in a common context of signaling-regulatory network that correlates with cell morphological features. They identified several pathways and associated transcription factors that their expression levels correlate with specific cell morphological features. The work thus has two main contributions. First, it provides a network of signaling pathways and regulons that may affect the morphological features of breast cancer cells. Second, the computational procedure can be general to study other systems.
\*Main comments***
3.1 I assume that in all analyses using the packages listed in the manuscript, some parameters need to be selected. The authors need to provide these details, and discuss whether the results are robust against parameter choice (at least to certain degree).
R3.1 We thank the reviewer for this comment. Parameters need to be selected in WGCNA and PCSF. In WGCNA they are selected based on the guidance given by the authors of the package, little significant variation in the results was observed when these were changed (i.e. the make-up of the gene expression modules naturally changed, but the processes enriched in the modules correlated to cell shape were the same).
PCSF is a more sensitive step because the best solutions to the sub-network identification problem are observed when the network edge weights are permuted over a number of iterations. Following this, the union of the produced array of networks is taken to be the solution. Obviously, biology is an inherently noisy system and so this formulation of the PCSF algorithm can capture latent network architecture that the deterministic variation cannot. This introduces extra parameters based on the requirement to introduce random noise to the network, along with the standard PCSF parameters (seen here: https://rdrr.io/github/IOR-Bioinformatics/PCSF/man/PCSF_rand.html) that are used to take into account of user variations in network degree distribution, edge-weight distribution, etc. It is normal for some tuning of parameters to be required for users to tailor their PCSF to their supplied network. We used degree distribution to gauge whether our network appeared to be of a biological ‘scale-free’ distribution and selected parameters based on that. This provides an affirmation that our resulting network is consistent with how we understand the topology of biological networks, and as a result the parameters selected are not arbitrary.
Nonetheless, we also tested variations in these parameters and found that although levels of significance in our validation would vary, the trends apparent from our validation did not (i.e., that targeting kinases within our network produced a larger effect on cell shape than those outside). From this we were assured that our conclusions mentioned in the discussion were robust to parameter selection. All details of parameters used are currently in our gitlab page, but we will additionally include them in the methods section.
3.2 Cells show some degree of heterogeneity both in cell expression and morphological features, which can be affected by many factors. Wu et al. (Sci Adv 2020, 6 (4): eaaw6938) identified several subgroups of MD-MBA-231 cells with persistent (over generations) distinct morphology, expression profiles, and metastasis potential. Another possible main factor to cell morphology heterogeneity is cell cycle stage. I understand that the analyses in this work are limited by the types of data available, for example, the expression data are largely bulk. One exception might be the data shown in Fig 5. Besides giving the fold changes after kinase inhibitor treatment, the authors may also analyze the variance of cells before and after treatment to estimate the relative extent of cell-cell heterogeneity relative to the effect due to treatment.
R3.2 We thank the reviewer for the comment and suggestion. We will perform such an analysis and include this point in the discussion. However, to reassure the reviewer, we are not concerned about this affecting our analysis in a major way as, in data from high content microscopy experiments such as the ones we used, hundreds of cells are sampled and the resulting quantified phenotypes are represented by the average from single cells, after removing outliers. Similarly in the bulk RNAseq experiments the dominant cell phenotype/expression profile would be mainly represented in the data. We are therefore reasonably confident that both sets of data used from each cell line indeed represented the most common phenotype for that cell line.
3.3. As related to point 2, In Fig. 1B, I am surprised that cell cycle only correlates with cell area significantly, while one knows that cells undergo dramatic change during cell cycle. For example, cells would turn to be roundish for mitosis. How would the authors explain the results? Is it possible that there is sampling bias towards interphase cells?
R3.3 We thank the reviewer for this comment and apologise for the confusion. The y axis of Fig.1B relates to gene expression modules identified in the expression data. These were named based on any informative term that could be associated with the genes within the modules as implemented by gene set enrichment. The goal was to provide more informative names than the default module names that are based on colours. ‘Cell cycle’ as a term in Reactome is a particularly generalisable gene set and was applied to the gene expression module in question because it was the only informative term identified for it. This singular gene expression module does not represent all transcriptomic activity associated with the cell cycle process. Indeed, the term ‘Cell cycle’ was also enriched in the ‘Hedgehog off-state’ gene expression module (Supplementary table 5). As the enrichment is based only on the genes: HAUS8;MCM8;NCAPH2;MIS12;BIRC5;CENPM;SPDL1;FBXO5;TYMS;TUBB4A, which are not necessarily the major cell cycle-relevant genes, we agree that the name of the specific module is not ideal and can cause confusion so we will rename this module. We will also go over the naming of all the modules to ensure that the names are indeed representative of the module functions.
\*Minor comments***
3.4 In Fig 1B, I have trouble to understand the biological relevance of some module names, like "Green", "indianred4"?
R3.4 Our pipeline uses WGCNA which constructs gene expression modules completely from gene expression data. We named modules based on terms we could find associated with the genes within a module. Some modules did not have any informative terms associated with them and so we opted to keep the default name of those modules that WGCNA supplies (based on colours). We will attempt to make this clearer in our revised manuscript, by adding a better explanation, and renaming these modules to something that makes it clear that we could not assign a clear function such as non-annotated (NA) module 1,2,3 etc.
3.5 Fig 3B: I can't find a detailed explanation on how the combined score was calculated.
R3.5 Thank you for pointing this out. This is described in Chen et al. 2013 as part of the enrichR package for gene set enrichment analysis. We will add this detail in the methods section under “Quantification and Statistical Analysis“.
3.6 Some of the cell features in Fig 5A are not in Fig 1. Are they from the same analysis? Any explanation?
R3.6 As the two datasets were acquired in two completely different studies there isn’t a 1-1 correspondence of the phenotype features, however several of them essentially represent the same phenotype. For example, in Fig 5., cytoplasm area, cytoplasm perimeter, nucleus area, nucleus length, nucleus width and nucleus perimeter, are analogous to features in Fig.1, such as cell area, cell width to length, nucleus area, nucleus width to length. The intersection between the features in these two datasets is not exact however, and we use the features in Fig.5 not used in the network construction as a negative control. This allows us to show that our network is phenotype-specific to the morphology features it was trained on. We will clarify this in the manuscript.
3.7) It is interesting that the authors have identified a number of pathways known to be related to mechanosensing. Does the Hippo-YAP/TAZ pathway appear in their analysis?
R3.7 Yes, YAP1 is also significantly highly ranked in our network propagation of activated transcription factors in Fig.4 in both luminal- and basal- shaped cell lines. Furthermore, since submitting we have been experimenting with identifying subnetworks of our regulatory network using maximum-flow. Here we assess the interaction between the Rap1 module (given its centrality to our discussion) with NFkB and what is the most efficient ‘flow’ of information between these two nodes given our network. To our interest, we identify LATS2, DVL1 (genes within the Rap1 module), YAP1 and TAZ as key mediating factors between these nodes. This implicates the Hippo-YAP/TAZ pathway as being of particular importance in the interface of our identified gene expression module and our derived signalling network. As an illustration of this we include here one of the preliminary networks derived from this analysis.
Figure - Network describing maximum flow (top 20 edges) between Rap1 signaling module as the source node and NFKB1 as the target node. The super-node representing the gene expression module is coloured red (with the interface nodes used to embed it in the signaling network coloured blue) and NFKB1 coloured azure. Edge thickness indicates weight, which was used as the maximum capacity used in the max flow calculation.
We will go over the figures and move barplots and more technical information to the supplement to make space for more figures of this nature that better illustrate the processes involved in the regulation of cell shape as derived from our analysis.
Reviewer #3 (Significance):
Extensive studies link cell morphological features and cell expression states, with some important work from one of the authors (Chris Bakal). This topic gains further interest recently. For example, Wu et al. (Sci Adv 2020, 6 (4): eaaw6938) demonstrated that cell shape encodes metastasis potential. Wang et al. (Sci. Adv. 2020 6 (36): eaba9319) traced cell dynamics in cell feature space. Given the context, the work of Barker et al. is a timely study to establish a cell shape-signaling network from integrated analysis of several different types of data. While some previous studies have related the NFkB network and cell morphology, this work further provides unbiased analysis on the relation between cell morphological features and multiple pathways/transcription factors. It is interesting, for example, that the study identifies the correlation between the Rap1 pathway and cell morphology, which was not well studied previously. As the authors acknowledged, there are some limitations of their approach. For example, the relations identified are correlative instead of causal without further verification. The resultant network may have sampling bias. Despite these limitations, I suggest that this work will be a nice contribution to the field and can provide a basis for further studies.
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Referee #3
Evidence, reproducibility and clarity
Summary
In this work Barker et al. used computational approaches to analyze several existing data sets (including morphology and expression) in a common context of signaling-regulatory network that correlates with cell morphological features. They identified several pathways and associated transcription factors that their expression levels correlate with specific cell morphological features. The work thus has two main contributions. First, it provides a network of signaling pathways and regulons that may affect the morphological features of breast cancer cells. Second, the computational procedure can be general to study other systems.
Main comments
1) I assume that in all analyses using the packages listed in the manuscript, some parameters need to be selected. The authors need to provide these details, and discuss whether the results are robust against parameter choice (at least to certain degree).
2) Cells show some degree of heterogeneity both in cell expression and morphological features, which can be affected by many factors. Wu et al. (Sci Adv 2020, 6 (4): eaaw6938) identified several subgroups of MD-MBA-231 cells with persistent (over generations) distinct morphology, expression profiles, and metastasis potential. Another possible main factor to cell morphology heterogeneity is cell cycle stage. I understand that the analyses in this work are limited by the types of data available, for example, the expression data are largely bulk. One exception might be the data shown in Fig 5. Besides giving the fold changes after kinase inhibitor treatment, the authors may also analyze the variance of cells before and after treatment to estimate the relative extent of cell-cell heterogeneity relative to the effect due to treatment.
3) As related to point 2, In Fig. 1B, I am surprised that cell cycle only correlates with cell area significantly, while one knows that cells undergo dramatic change during cell cycle. For example, cells would turn to be roundish for mitosis. How would the authors explain the results? Is it possible that there is sampling bias towards interphase cells?
Minor comments
4) In Fig 1B, I have trouble to understand the biological relevance of some module names, like "Green", "indianred4"?
5) Fig 3B: I can't find detailed explanation on how the combined score was calculated.
6) Some of the cell features in Fig 5A are not in Fig 1. Are they from the same analysis? Any explanation?
7) It is interesting that the authors have identified a number of pathways known to be related to mechanosensing. Does the Hippo-YAP/TAZ pathway appear in their analysis?
Significance
Extensive studies link cell morphological features and cell expression states, with some important work from one of the authors (Chris Bakal). This topic gains further interest recently. For example, Wu et al. (Sci Adv 2020, 6 (4): eaaw6938) demonstrated that cell shape encodes metastasis potential. Wang et al. (Sci. Adv. 2020 6 (36): eaba9319) traced cell dynamics in cell feature space. Given the context, the work of Barker et al. is a timely study to establish a cell shape-signaling network from integrated analysis of several different types of data. While some previous studies have related the NFkB network and cell morphology, this work further provides unbiased analysis on the relation between cell morphological features and multiple pathways/transcription factors. It is interesting, for example, that the study identifies the correlation between the Rap1 pathway and cell morphology, which was not well studied previously. As the authors acknowledged, there are some limitations of their approach. For example, the relations identified are correlative instead of causal without further verification. The resultant network may have sampling bias. Despite these limitations, I suggest that this work will be a nice contribution to the field and can provide a basis for further studies.
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Referee #2
Evidence, reproducibility and clarity
The authors combine single cell morphology and gene expression data to identify signaling activities implicated in the control of cellular morphogenesis. They describe a reasonable bioinformatics pipeline from gene expression shifts between two morphological phenotypes to pathways, then to common transcription factors to signaling. As far as I can assess the situation (I am not familiar with all the tools they use) the proposed pipeline works convincingly. However, I am concerned that the logic underlying this analysis is only partially valid. The link between signaling and morphology may be more direct than via TF-based gene expression regulation. Many signals (and many of the kinases the authors test for validation) are implicated in morphology control as direct upstream regulators of cytoskeleton dynamics and adhesion. This also applies to the GTPase Rap1, which the authors fish out as the most differentially expressed signal between two types of morphologies. In addition to the indirect effect of Rap1 on morphology via NFKB regulation suggested by the authors, Rap1 will affect morphology probably very directly through activation of Rac -> F-actin and RIAM -> nascent adhesions. At minimum, the authors should discuss this complexity as a caveat of their approach. And dependent on the impact the authors hope to have with this story, I believe they should experimentally resolve the ambiguity of direct vs indirect signaling for some of their key interpretations.
In defense to the presented premise, the authors start out by looking for correlation between gene expression and morphology, and they find some signal. Correlation analysis, especially in large data sets, tends to be pretty robust and specific, even on presence of strong confounders. Thus, even though the correlation expression-morphology, which points indirectly at morphology-regulating signaling modules, is likely to be super-imposed by direct morphology-regulating signaling pathways the proposed approach will not be able to detect, the presented analysis is valuable, in principle.
That said, I have a number of substantial concerns also with the implementation and presentation of the approach. First, on the presentation side, for a paper that talks about cell morphology it is strange to have not a single figure panel showing an image of cells, or at least cell outlines. As a reader I would like to get visual impression of how different a high vs low Rap1 gene expresser is, for example. Along the same lines, it is not quite clear to me when the authors collate entire cell lines into a single phenotype, do they switch then to population-based analysis? That is, for example the volcano plots in 2B,C are they representing an average gene expression shift? How heterogeneous are the morphological signals? Are the correlations between gene expression and morphology computed with single cell data as the basis? Could the volcano plots be sharpened by accounting for the single cell variation in morphology instead of lumping the cells into two morphological classes? On the back end of the paper, when the authors apply kinase inhibitors to validate some of the claimed pathways, it would be nice for the reader to see the morphological effects of these inhibitors. And to relate the kinase induced shifts to the morphological heterogeneity that is the basis for the study driving, initial correlation analysis? At the end of the day, the proof is in the pudding.
Finally, cell morphology regulation is a pretty foundational process of life. One therefore wonders whether the pathways the authors pulled out of their analysis work also in other cell types, beyond breast cancer cells? What if they pooled data from different cell types that cover the morphological state space more broadly?
Significance
The premise of this manuscript is very exciting and interesting: Is it possible to identify from a correlation of cell morphology and single cell gene expression the underlying cell signaling states that control morphology? Answers to this will begin to shed some light on the black box relation of morphology as an informant of cell states, which has been exploited by pathologists, physiologists, and cell biologists for more than a century, and which has seen a sharp revival recently thanks to deep learning, which is exceedingly good at finding correlations between data patterns.
This paper would have a broad audience in quantitative cell biology, systems biology, and perhaps also life data science and cancer (although the cancer aspect is marginal).
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Referee #1
Evidence, reproducibility and clarity
The submitted manuscript 'Identification of phenotype-specific networks from paired gene expression-cell shape imaging data' of Barker et al. uses a convolute of different bioinformatics tools (see Key Resource Table) to analyze reported RNA sequencing data and to correlate derived pathways with imaging features of breast cancer cell lines based on specific pathway constructions. The thin red line of the data presentation in the manuscript is not obvious.
Major concerns:
- The main biological 'finding' of the study RAP1 'as a potential mediator between the sensing of mechanical stimuli and regulation of NFkB activity' is reported and therefore the assumption 'how exactly extra-cellular mechanical cues are sensed by the cell and passed on to NFkB in breast cancer is not understood' is misleading. Please review: https://www.nature.com/articles/ncb2080 (human breast cancers with NF-κB hyperactivity show elevated levels of cytoplasmic Rap1. Similar to inhibiting NF-κB, knockdown of Rap1 sensitizes breast cancer cells to apoptosis) https://pubmed.ncbi.nlm.nih.gov/17510404/ (RAP1 is a crucial element in organizing acinar structure and inducing lumen formation), and https://pubmed.ncbi.nlm.nih.gov/21429211/. Besides, Fig. 2 and 3 are unrelated to this main statements.
- The spotted RAP1 (by TFs JARD2 and RUNX2) finding is not obvious without Fig. 4 results, a network propagation of functional TFs in differentially activated processes (basal vs. luminal) in the cell shape regulatory network. Please show that RAP1 could be not identified without the network based on TF and DEG only.
- More complex fluorescence phenotypes are available and do not match the complexity of the RNASeq data, data input and pathway construction with only 10 simple cell shape features. Conversely, relative 'monoclonal' breast cancer cell lines may are the only application for this workflow. Image features Fig. 1 and 5 do not match, with Fig. 5 being a rather indirect 'proof' of usability.
- Fig. 1a has not achieved a visual descriptive state and asking a lot.
Significance
The 'Review Commons' efficiently facilitates the reviewing process for the corresponding journals due to the broader 'audience'. On the other hand, authors face less restrictions and pressure for the same reason. Although I really like the idea of pulling the reviews upstream into the preprint process, I would like to answer here also with a kind of pre-review to avoid entering partly immature manuscript to 'Review Commons'. Review Commons might install an automated 'sanity check' of manuscripts in the future to keep the quality of submissions higher?
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Reply to the reviewers
Review Commons Reviews for Refereed Preprint RC-2021-00693
Ferrari G. et al., DLL4 and PDGF-BB regulate migration of human iPSC-derived skeletal myogenic progenitors.
Reviewer #1 (Evidence, reproducibility and clarity): Summary:
The paper presented by Ferrari et al., aims to improve the migration capacity of hiPSC- derived myogenic progenitors. For this purpose, the authors used a previously published well characterized hiMPs model and focussed on the modulation of NOTCH and PDGF signaling pathways. The rational to target these pathways was based on muscle cells migrations molecular events observed during developmental described in the literature.
Major comments: Are the key conclusions convincing?
This is a very interesting paper. Few clarifications as suggested below need to be done before being fully convincing. Enrichment test and heat maps and the network analysis are not well explained in terms of which genes were selected and why, and in terms of which gene set were selected and why. In some cases, the information may be given in the paper, but it is not easy for the reader to find it. It should be stated more clearly. For example, in Fig2C why these eight were chosen for the heat maps and why not other genes known to be involved in myogenesis, cell migration etc. Similar comment for figure 3 A, D and G. Another example, in Fig 2E, on what basis are some gene sets chosen to be shown in this figure when there are many more significant in the supplementary table.
We thank the Reviewer for their positive feedback and for this comment. Although some answers to the queries could be found within the figure legends, we agree that figures could have been more self-explanatory, and we will amend them accordingly. We will also add additional information into the main text to clarify those specific points.
In response to the specific queries:
- All enrichment heat maps were generated from GO lists or KEGG pathways.
- 2C: these were chosen instead of other myogenic or cell migration markers for consistency with our previous study (Figure 2C in Gerli et al Stem Cell Reports 2019).
- 3A, D, G: details of the GO lists used to generate heat maps were available in the relative figure legend.
- 2E: enrichment pathways – we listed pathways shared between at least 2 of the three groups and with relevance to cellular migration.
Figure 4F is impossible to interpret without a clear description of how the subnetwork is extracted, was a list of gene list submitted to string, if so which genes and why? Secondly, why are there many nodes with no edges? Is it all of the nodes that are in that GO-Term, if so it needs to be clarified? Was this the most strongly deregulated go-Term according to string analysis?
We thank the Reviewer for this comment. This specific GO list was selected for its highly relevant title/topic, i.e.: “positive regulation of cell migration”. Details on this point could also be found in the specific figure legend, where we specified how the network is extracted and constructed. There are several nodes with no edges as the edges represent predicted functional association and therefore, a lack of edges suggests a lack of interaction.
Figure 4 B, C, D and E: (1) The authors should clarify what figure 4B is? Is 1,2,3,4 different time point? Treated or untreated cells?
We apologise with the Reviewer for not having provided enough information on this point. 1,2,3 and 4 are four sequential time points of untreated cells. We will amend the figure to make this clearer.
(2) Figure C: Is the graph showing the cell distribution of both treated and untreated cells? If yes is it possible to give a different shape for the control cells and see if indeed more control green shape would be observed in this plot? (In the supplementary data there is the distribution showing the treated v untreated, but the clusters are not visible)
We thank the Reviewer for this helpful comment. We agree that this will increase the quality of the figure. We will distinguish treated and control cells within figure 4C by replacing dots with different shapes for treated and untreated samples.
(3) Would it be possible to take some of the parameters in Figure 4D and show the distribution in treated vs untreated and perform the statistical analysis? (eg is there a significant difference for the parameter total distance between control and treated?). Or, may be just show some of the results in figure S4C and E in the main text.
We thank the Reviewer for this comment. We agree that it will be better to move S4C into the main figure and we will action this point in the revised version of the manuscript.
(4) Why pooling the 3 independent experiment together? Looking at the data in Figure S4, it seems that one treated sample is very similar to the control, thus weakening the conclusion. The replicates in this figure are biological replicates. Yet the papers present 4/5 different cell lines, so why only 3 of them are used here? Is there some explanation regarding the outsider (cell line age, number of division etc). Might be worth adding data from the other cell lines (1 or 2 more).
We thank the Reviewer for this point. The experiment shown in figure S4E has been performed with one cell line (N5) and independent experimental replicates were assessed for the statistical analysis. We are not sure why there appears to be an outlier in some cases, and this is why it was important to replicate this experiment three times. However, we will also repeat this experiment with another cell line applying more stringent conditions to strengthen this point.
(5) Figure 4 H and I: What are the statistic actually comparing: treated v untreated for each cell lines or different cell lines against each other? If the former, then how is it possible to have a 139 fold change with such a weak p value of 0.042? If the latter, then why is a p-value given for each of the 3 cell lines? Also, the number and source of replicates is unclear - N=3 is stated, so was each cell line done in triplicate? If so, how many fields per replicate?
We are happy to clarify this point for the Reviewer. The statistical analysis compares treated vs. untreated samples within the same genotype. The high fold change observed is likely due to the large standard deviation of the dataset, which was also highlighted as raw data in the figure panel (bottom part of each picture in white colour font). For this reason, we have repeated this experiment multiple times and validated it across three independent cell lines.
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. It would important to also show the migratory capacity of these cells in vivo.
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. Human muscle cells engraftment and tracking in immunodeficient mice could be easily done. Engrafted muscle can be harvested 2-3 weeks after engraftment, and measurement of the distance from the engraftment point could be done (Site of injection could be labelled with tattoo die). This would be a month/month and half of work. Immunodeficient mice would cost around £1500 (n=6 mice per group => total of 12 mice) plus the cost of housing.
Are the data and the methods presented in such a way that they can be reproduced? Are the experiments adequately replicated and statistical analysis adequate? See comments in first paragraph. The authors should probably be able to answer easily to the different concerns raised above.
We thank the Reviewer for these comments. We agree that the suggested in vivo experiment might strengthen our work and we are currently sourcing all required materials to perform it. Additionally, we will perform a similar, quasi-vivo, experiment to study migration in a species-specific setting by delivering cells in 3D models in vitro (e.g. Maffioletti SM et al., Cell Reports 2018). This strategy will provide a solid alternative to the in vivo assay, in the eventuality that the xenogeneic setting will limit the resolution of the proposed transplantation experiment.
Minor comments: typo "Onthology" should be "Ontology" in figure 2E. Some of the data in Figure S4E should be moved to the main text.
Thank you for highlighting these minor comments. We will correct the typo and move data from figure S4 into the main figure 4.
Reviewer #2 (Evidence, reproducibility and clarity): In this manuscript, Ferrari and colleagues provide solid data indicating that the Notch ligand DLL4 and PDGF-BB regulate the migration of myogenic progenitors derived from human pluripotent stem cells (PSC). These studies built from recent work by the same group (Gerli et al, Stem Cell Reports, 12:461, 2019), in which the authors documented that Notch and PDGF-BB signaling enhances migration and expression of stem cell markers while inducing perivascular cell features in muscle satellite cells. Here the authors perform similar in vitro studies in PSC-derived myogenic progenitors and conclude that the same effect is observed in this population of cells. The results are clear and well presented.
Throughout the manuscript, the authors emphasize the importance of such findings for the future therapeutic application of a PSC-based therapy to treat patients with muscular dystrophy since multiples skeletal muscles need to be targeted in this group of diseases. Unfortunately, the authors do not provide transplantation data. The results would be highly meaningful if they show that observed in vitro changes (transcriptomes and chamber assay) result in meaningful migration in vivo using the systemic delivery, but as it is, the data do not support the claims and conclusions.
We thank Reviewer 2 for their comments. We were pleased to read that they found our study and data solid, clear and well presented. Although we agree with the Reviewer that in vivo evidence would strengthen our findings, we would like to highlight that our study did not aim to be a translational investigation of the therapeutic potential of treated hPSC derivatives for muscle cell therapy (we believe our manuscript’s title reflects this). We see this work more as a foundational study to establish the required evidence for future, follow up transplantation studies focused on the therapeutic potential of this approach (something requiring a dedicated project, funding and months/years of work).
Moreover, we believe that xenogeneic transplants are of limited use to investigate a complex species-specific phenomenon such as transendothelial cell migration. For this very reason we moved back to intraspecific transplantsin past studies (e.g.. Tedesco et al Sci Transl Med 2012). However, as a key aim of our study is to obtain data specific to human cells and given that we already performed mouse-in-mouse in vivo intra-arterial delivery experiments using DLL4 and PDGFBB treated primary cells in Gerli et al. Stem Cell Reports 2018, we are therefore proposing and planning to:
- Test transendothelial migration with another quasi-vivo microfluidic assay orthogonal to the reported transwell experiments. This will model intraspecific (i.e., human-in-human) transendothelial migration under flow conditions.
- Assess evidence of migration in human 3D muscles setting up a novel invasion assay in our in vitro 3D muscle models.
- Perform intramuscular delivery of treated vs. untreated cells as per Reviewer 1 request to assess migration in skeletal muscle in vivo. This approach will optimise in vivo experiments in a 3Rs compliant fashion, avoiding invasive procedures in animals to study intravascular delivery.
Reviewer #2 (Significance): Significance is limited if only in vitro data are provided. However if the authors are able to show enhanced engraftment upon systemic transplantation of human PSC-derived myogenic progenitors upon DLL4 and PDGF-BB treatment, the significance would be high.
Please see our reply to the previous point.
In terms of existing literature, there are publications reporting systemic delivery of murine PSC-derived myogenic progenitors as well as transcriptome and in vitro migration studies. It would probably be appropriate to cite them.
We apologies to the Reviewer for this oversight. We will add the following papers which include systemic delivery of murine PSC-derived myogenic progenitors as well as transcriptome and migration studies: Matthias N et al., Exp Cell Res 2015; Incitti T et al., PNAS 2019.
If systemic engraftment is observed, the manuscript would be of interest to the skeletal muscle and stem cell biology/regenerative medicine community.
Please see our reply to the initial point.
Reviewer #3 (Evidence, reproducibility and clarity):
In this manuscript, the authors exploited the signal-mediated activation of NOTCH and PDGF pathways, by one week-long delivery of DLL4 and PDGF-BB to cultures of hiPSC-derived myogenic progenitors in vitro, to improve their migration ability. They performed transcriptomic and functional analyses across human and mouse primary muscle stem cells and human hiPSC-derived myoblasts, including genetically corrected hiPSC derivatives, to show that DLL4 and PDGF-BB treatment modulates pathways involved in cell migration, including enhanced trans-endothelial migration in transwell assays.
The increased migratory ability, and in particular enhancing extravasation, is a fundamental property required for optimal performance of hiPSC myogenic derivatives, upon their intravascular delivery; hence, the finding reported here are of extremely high potential interest in term of solution of one of the major bottle-neck of cell therapy. However, there are important issues that need to be resolved by the authors with additional experimentation, that I recommend performing, in order to improve this manuscript.
We sincerely thank the Reviewer for acknowledging the extremely high relevance and potential of our paper for muscle gene and cell therapies and for providing constructive feedback to improve our manuscript.
1) The most critical issue here is that the authors fail to provide evidence that DLL4/PDGF-BB-treated cultures of hiPSC-derived myogenic progenitors do not lose their myogenic potential and are able to form myotubes, upon interruption of treatment. It would be also important to determine when (how many days after withdrawal of DLL4/PDGF-BB) the full myogenic properties of these cells are recovered. From the RNAseq datasets shown by the authors, it appears that DLL4/PDGF-BB-treated hiPSC-derived myoblasts do not express the key genes of myogenic identity (MyoD) and early differentiation (myogenin), while expressing genes of mesenchymal/vessel-derived lineages. It is imperative that the authors show that these changes are reversible, upon withdrawal of DLL4/PDGF-BB. This should be show by an unbiased transcriptomic analysis (RNAseq) of hiPSC-derived myoblasts after withdrawal of DLL4/PDGF-BB, that should be integrated with functional evidence showing that these cells can resume their ability to form differentiated myotubes, upon exposure to myogenic culture cues in vitro.
We thank the Reviewer for this comment. We agree that this is an important and feasible experiment which will add important information to our work. We performed similar work in our previous study and already observed phenotype reversion of treated cells upon release of the stimuli within a few passages in cultures. However, we agree that this requires systematic assessment and quantification. To this aim, we will assess the reversibility of the DLL4 & PDGF-BB effect by stopping treatment at day 7 and then assessing skeletal myogenic differentiation capacity of target cells at sequential passages and time points post-treatment. Analysis of the differentiation index at different time points will provide functional evidence on the myogenic potential of hiPSC-derived myogenic progenitors post-withdrawal of DLL4 & PDGF-BB. We believe that the Reviewer’s suggestion for transcriptomic analysis via RNA-seq might be overly costly for the purpose of identifying the myogenic potential of treated cells post-withdrawal of treatment, and that qPCR panels alongside immunofluorescence staining may be sufficient.
2) A parallel evidence in vivo should be also provided, showing that DLL4/PDGF-BB-treated hiPSC-derived myoblasts do not express MyoD and myogenin when delivered intravascularly, but regain their expression after they have crossed the vessel endothelium and have entered the skeletal muscles.
We thank the Reviewer for suggesting this experiment. We agree that this would be a very interesting point to address; however, it might be very challenging to address this question with the proposed in vivo experiment. Nonetheless, we believe that with a combination of in vitro and in vivo assays we will be able to satisfactorily answer the question: Do DLL4 and PDGF-BB-treated myogenic progenitors re-gain myogenic potential upon entering skeletal muscle tissue? To this aim, we aim to analyse muscles following intramuscular transplantation of treated and untreated cells. Moreover, to model intra-vascular delivery and have high resolution imaging, we aim to adapt a microfluidic platform to perform trans-endothelial assays and selectively differentiate cells that successfully cross the blood vessel layer. Although likely to be very challenging, we will attempt to capture or stain those very cells in order to assess the expression of myogenic markers as requested by the Reviewer.
If these experiments could firmly demonstrate that DLL4/PDGF-BB-treatment reversibly promotes migratory properties of hiPSC-derived myoblasts (as predicted, but not demonstrated in previous works from the same group, using mouse or human primary muscle stem cells - Cappellari et al. 2013; Gerli et al. 2019), then this work could be a great interest in term of basic and translational biology and clearly suitable for publication in a top journal.
We thank the Reviewer for this constructive feedback and for seeing the great potential of our work in terms of basic and translational biology. We assume there was a typo in the sentence in brackets with a missing “as” (“..not demonstrated as in previous work...”): we indeed demonstrated the effect of DLL4 and PDGFBB in vivo extensively in our previous work.
Other points:
- Fig. 2A. it looks like there are some outlier RNAseq sample replicates that might negatively impact at the statistical level on the subsequent analysis. This issue is likely due to the heterogeneity of the samples (both untreated and treated) and could be resolved by replacing outlier samples with new replicates.
We thank the Reviewer for this comment. Although we agree that replacing those samples with new replicates might improve our statistical analyses, this will be financially challenging at this stage and perhaps also not completely reflecting the real variability of the experimental setup.
- Along the same line as above, sample heterogeneity following treatment might be resolved by a better understanding of optimal doses of DLL4/PDGF-BB and time of exposure, which I recommend the authors to define by additional experiments.
We thank the Reviewer for this comment. This is a potentially interesting experiment, which we have not performed as we took advantage of previous knowledge and dose-response on primary mouse and human myoblasts. Overall, we believe that this experiment might not be strictly required at this stage, given that we have already solid evidence of response in hiMPs with a defined concentration and exposure time of DLL4 and PDGFBB.
Reviewer #3 (Significance):
If these experiments could firmly demonstrate that DLL4/PDGF-BB-treatment reversibly promotes migratory properties of hiPSC-derived myoblasts (as predicted, but not demonstrated in previous works from the same group, using mouse or human primary muscle stem cells - Cappellari et al. 2013; Gerli et al. 2019), then this work could be a great interest in term of basic and translational biology and clearly suitable for publication in a top journal and could be interesting for a wide audience in regenerative medicine.
We thank the Reviewer once again for this constructive feedback and for seeing the great potential of our work in terms of basic and translational biology, as well as for regenerative medicine.
Please note that the following statement will be added to the Acknowledgements section of our revised manuscript: "For the purpose of Open Access, the author has applied a CC BY public copyright licence to any Author Accepted Manuscript version arising from this submission. This work was supported by the Francis Crick Institute which receives its core funding from Cancer Research UK, the UK Medical Research Council, and the Wellcome Trust (FC001002)".
Once again, we sincerely thank all Reviewers for their positive, constructive and insightful comments, which motivate us to further improve our work. We also thank the Review Commons editorial team for guidance and assistance.
Prof. Francesco Saverio Tedesco, University College London and The Francis Crick Institute, London, UK.
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Referee #3
Evidence, reproducibility and clarity
In this manuscript, the authors exploited the signal-mediated activation of NOTCH and PDGF pathways, by one week-long delivery of DLL4 and PDGF-BB to cultures of hiPSC-derived myogenic progenitors in vitro, to improve their migration ability. They performed transcriptomic and functional analyses across human and mouse primary muscle stem cells and human hiPSC-derived myoblasts, including genetically corrected hiPSC derivatives, to show that DLL4 and PDGF-BB treatment modulates pathways involved in cell migration, including enhanced trans-endothelial migration in transwell assays. The increased migratory ability, and in particular enhancing extravasation, is a fundamental property required for optimal performance of hiPSC myogenic derivatives, upon their intravascular delivery; hence, the finding reported here are of extremely high potential interest in term of solution of one of the major bottle-neck of cell therapy. However, there are important issues that need to be resolved by the authors with additional experimentation, that I recommend performimg, in order to improve this manuscript.
1) The most critical issue here is that the authors fail to provide evidence that DLL4/PDGF-BB-treated cultures of hiPSC-derived myogenic progenitors do not lose their myogenic potential and are able to form myotubes, upon interruption of treatment. It would be also important to determine when (how many days after withdrawal of DLL4/PDGF-BB) the full myogenic properties of these cells are recovered. From the RNAseq datasets shown by the authors, it appears that DLL4/PDGF-BB-treated hiPSC-derived myoblasts do not express the key genes of myogenic identity (MyoD) and early differentiation (myogenin), while expressing genes of mesenchymal/vessel-derived lineages. It is imperative that the authors show that these changes are reversible, upon withdrawal of DLL4/PDGF-BB. This should be show by an unbiased transcriptomic analysis (RNAseq) of hiPSC-derived myoblasts after withdrawal of DLL4/PDGF-BB, that should be integrated with functional evidence showing that these cells can resume their ability to form differentiated myotubes, upon exposure to myogenic culture cues in vitro.
2) A parallel evidence in vivo should be also provided, showing that DLL4/PDGF-BB-treated hiPSC-derived myoblasts do not express MyoD and myogenin when delivered intravascularly, but regain their expression after they have crossed the vessel endothelium and have entered the skeletal muscles. If these experiments could firmly demonstrate that DLL4/PDGF-BB-treatment reversibly promotes migratory properties of hiPSC-derived myoblasts (as predicted, but not demonstrated in previous works from the same group, using mouse or human primary muscle stem cells - Cappellari et al. 2013; Gerli et al. 2019), then this work could be a great interest in term of basic and translational biology and clearly suitable for publication in a top journal.
Other points:
- Fig. 2A. it looks like there are some outlier RNAseq sample replicates that might negatively impact at the statistical level on the subsequent analysis. This issue is likely due to the heterogeneity of the samples (both untreated and treated) and could be resolved by replacing outlier samples with new replicates.
- Along the same line as above, sample heterogeneity following treatment might be resolved by a better understanding of optimal doses of DLL4/PDGF-BB and time of exposure, which I recommend the authors to define by additional experiments.
Significance
If these experiments could firmly demonstrate that DLL4/PDGF-BB-treatment reversibly promotes migratory properties of hiPSC-derived myoblasts (as predicted, but not demonstrated in previous works from the same group, using mouse or human primary muscle stem cells - Cappellari et al. 2013; Gerli et al. 2019), then this work could be a great interest in term of basic and translational biology and clearly suitable for publication in a top journal and could be interesting for a wide audience in regenerative medicine.
Expertise of this reviewer:
Muscle regeneration; Muscular Dystrophies; Signaling and Epigenetics
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Referee #2
Evidence, reproducibility and clarity
In this manuscript, Ferrari and colleagues provide solid data indicating that the Notch ligand DLL4 and PDGF-BB regulate the migration of myogenic progenitors derived from human pluripotent stem cells (PSC). These studies built from recent work by the same group (Gerli et al, Stem Cell Reports, 12:461, 2019), in which the authors documented that Notch and PDGF-BB signaling enhances migration and expression of stem cell markers while inducing perivascular cell features in muscle satellite cells. Here the authors perform similar in vitro studies in PSC-derived myogenic progenitors and conclude that the same effect is observed in this population of cells. The results are clear and well presented.
Throughout the manuscript, the authors emphasize the importance of such findings for the future therapeutic application of a PSC-based therapy to treat patients with muscular dystrophy since multiples skeletal muscles need to be targeted in this group of diseases. Unfortunately, the authors do not provide transplantation data. The results would be highly meaningful if they show that observed in vitro changes (transcriptomes and chamber assay) result in meaningful migration in vivo using the systemic delivery, but as it is, the data do not support the claims and conclusions.
Significance
Significance is limited if only in vitro data are provided. However if the authors are able to show enhanced engraftment upon systemic transplantation of human PSC-derived myogenic progenitors upon DLL4 and PDGF-BB treatment, the significance would be high.
In terms of existing literature, there are publications reporting systemic delivery of murine PSC-derived myogenic progenitors as well as transcriptome and in vitro migration studies. It would probably be appropriate to cite them.
If systemic engraftment is observed, the manuscript would be of interest to the skeletal muscle and stem cell biology/regenerative medicine community.
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Referee #1
Evidence, reproducibility and clarity
Summary:
The paper presented by Ferrari et al., aims to improve the migration capacity of hiPSC- derived myogenic progenitors. For this purpose, the authors used a previously published well characterized hiMPs model and focussed on the modulation of NOTCH and PDGF signaling pathways. The rational to target these pathways was based on muscle cells migrations molecular events observed during developmental described in the literature.
Major comments:
- Are the key conclusions convincing? This is a very interesting paper. Few clarifications as suggested below need to be done before being fully convincing. Enrichment test and heat maps and the network analysis are not well explained in terms of which genes were selected and why, and in terms of which gene set were selected and why. In some cases, the information may be given in the paper, but it is not easy for the reader to find it. It should be stated more clearly. For example, in Fig2C why these eight were chosen for the heat maps and why not other genes known to be involved in myogenesis, cell migration etc. Similar comment for figure 3 A, D and G. Another example, in Fig 2E, on what basis are some gene sets chosen to be shown in this figure when there are many more significant in the supplementary table. Figure 4F is impossible to interpret without a clear description of how the subnetwork is extracted, was a list of gene list submitted to string, if so which genes and why? Secondly, why are there many nodes with no edges? Is it all of the nodes that are in that GO-Term, if so it needs to be clarified? Was this the most strongly deregulated go-Term according to string analysis? Figure 4 B, C, D and E:
(1) The authors should clarify what figure 4B is? Is 1,2,3,4 different time point? Treated or untreated cells?
(2) Figure C: Is the graph showing the cell distribution of both treated and untreated cells? If yes is it possible to give a different shape for the control cells and see if indeed more control green shape would be observed in this plot? (In the supplementary data there is the distribution showing the treated v untreated, but the clusters are not visible)
(3) Would it be possible to take some of the parameters in Figure 4D and show the distribution in treated vs untreated and perform the statistical analysis? (eg is there a significant difference for the parameter total distance between control and treated?). Or, may be just show some of the results in figure S4C and E in the main text.
(4) Why pooling the 3 independent experiment together? Looking at the data in Figure S4, it seems that one treated sample is very similar to the control, thus weakening the conclusion. The replicates in this figure are biological replicates. Yet the papers present 4/5 different cell lines, so why only 3 of them are used here? Is there some explanation regarding the outsider (cell line age, number of division etc). Might be worth adding data from the other cell lines (1 or 2 more).
(5) Figure 4 H and I: What are the statistic actually comparing: treated v untreated for each cell lines or different cell lines against each other? If the former, then how is it possible to have a 139 fold change with such a weak p value of 0.042? If the latter, then why is a p-value given for each of the 3 cell lines? Also, the number and source of replicates is unclear - N=3 is stated, so was each cell line done in triplicate? If so, how many fields per replicate?
- 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. It would important to also show the migratory capacity of these cells in vivo. -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. Human muscle cells engraftment and tracking in immunodeficient mice could be easily done. Engrafted muscle can be harvested 2-3 weeks after engraftment, and measurement of the distance from the engraftment point could be done (Site of injection could be labelled with tattoo die). This would be a month/month and half of work. Immunodeficient mice would cost around £1500 (n=6 mice per group => total of 12 mice) plus the cost of housing.
- Are the data and the methods presented in such a way that they can be reproduced? Are the experiments adequately replicated and statistical analysis adequate?
See comments in first paragraph. The authors should probably be able to answer easily to the different concerns raised above.
Minor comments:
typo "Onthology" should be "Ontology" in figure 2E. Some of the data in Figure S4E should be moved to the main text.
Significance
Describe the nature and significance of the advance, existing literature, audience: Generating iPSC cell lines with an improved capacity to migrate will be of high interest for the neuromuscular field, and could be a potential therapeutic strategy applicable for many neuromuscular disorders.
Muscle cell engraftment is quite challenging as the capacity of these cells to populate different muscles is very poor. Improving the cell migration, survival and proliferation may thus help to improve the muscle cell engraftment strategy.
Expertise:
I have an expertise in neuromuscular disorders, muscle stem cells (human and murine, in vitro and in vivo), as well as an expertise in omics analysis.
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Reply to the reviewers
Point-by-point response to reviewer comments
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
In the current manuscript, Millarte et al reports a novel role of Rabaptin5 in selectively clearing damaged endosomes via canonical autophagy. They have identified FIP200 as a novel interactor of Rabaptin5 under basal conditions using yeast-two hybrid screening and further confirmed the interaction of Rabaptin5 with FIP200 with immunoprecipitation. They next used Chloroquine and monitored colocalization of the Rabaptin5 with WIPI2, ATG16L1 and LC3B to demonstrate the potential interaction of Rabaptin5 with the autophagic machinery. They have primarily used Gal-3 as a marker of membrane damage after 30 minutes of Chloroquine treatment. In order to further elucidate the role of Rabaptin5 in autophagic induction mediated by Chloroquine, they have silenced Rabaptin5, FIP200, ULK1 and ATG13 and observed a decrease in the number of LC3 or WIPI2 autophagosome formation. Based on these observations they tested if Rabaptin5 interacts with ATG16L1 upon Chloroquine treatment and confirmed their interaction with potential interaction sites of both Rabaptin5 with ATG16L1 with IP. The authors confirmed the interaction of Rabaptin5 with ATG16L1 by complementing the KO line with the mutant form of Rabaptin5 containing alanine residues in its consensus motif. Finally, they have used Salmonella and SCV as a model to study the role of Rabaptin5 in endomembrane damage and monitored a 50% decrease in the removal of Salmonella in Rabaptin5 KO or KD cells.
Major concerns One of the major concerns is the membrane damage reported by chloroquine which is known to induce lysosomal swelling and further targeting of the swollen compartments to degradation by direct conjugation of LC3 onto single membrane as a form of non-canonical autophagy. The evidence regarding membrane damage by Gal3 colocalization on the Rabaptin5 vesicles is preliminary. As suggested by the authors the canonical autophagy pathway recognizing damaged membranes recruits also ALIX to the damaged membrane which was not observed in Supplementary Figure 2. The link to membrane damage by chloroquine and monensin with Rabaptin5 is not convincing as there is not sufficient evidence of membrane damage. In relation to this issue authors should consider using other damage markers as Gal8, p62 or NDP52 to provide additional claim with respect to membrane damage induced by chloroquine.
To expand on the question of CQ treatment damaging early endosomes, we also tested for Gal8 on Rabaptin5-positive enlarged endosomes and quantified the fraction of Rabaptin5-positive rings positive for Gal3 and Gal8 after 30 min of CQ treatment. We propose to include this data in Figure 2:
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We have tested the importance of Gal3 and p62 by siRNA-mediated knockdown where we found a robust inhibition of induction of WIPI2 puncta with CQ, but not with Torin1. Formation of LC3 puncta was less reduced, similar to knockdowns of FIP200, ATG13, or Rabaptin5.
We propose to add these knockdown experiments as a supplementary figure:
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One of the main claims here is that Rabaptin5 regulates the targeting of damaged endosomes to autophagy. Clearly, these are early endosomes as stated in the abstract. However, the evidence presented here showing these are early endosomes is not convincing. Analysing Gal3 and Gal8 positive vesicles that are Rabaptin5 positive and an early endosomal marker will be important in this context. For example, there need to be additional evidence showing that early endosomes are targeted to autophagy. Is the degradation of TfR affected by this targeting? Did the authors look at the effect of Bafilomycin A1? If this process affects exclusively early endosomes, it should be BafA1 independent. This will direct more into the cellular function of this process.
Rabaptin5 is a bona fide marker of Rab5-positive early sorting endosomes. As a control, we confirmed colocalization of Rabaptin5 with transferrin receptor, another endosomal marker, on CQ-induced rings (Fig. 2B). We now also analyzed swollen endosomes with triple-staining for Rabaptin5, transferrin receptor, and Gal3 as shown in this gallery (30 min CQ, as in Fig. 2). All Rabaptin5-positive swollen endosomes (rings) were positive for transferrin receptor and ~80% for mCherry-Gal3.
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We further tested transferrin receptor levels with and without CQ. Since CQ inhibits autophagic flux, this assay may not be very sensitive. Nevertheless, we found a significant reduction of ~15% and ~30% after overnight incubation with CQ in parental HEK293A cells and in Rbpt5-KO cells re-expressing wild-type Rabaptin5, resp., but no reduction in Rbpt5-KO cells expressing the Rabaptin5-AAA mutant defective in binding to ATG16L1:
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As to the effect of BafA1, see our general response on top. The osmotic effect of CQ or Mon on endosomes that leads to membrane breakage requires an acidic pH. Preincubation with BafA1 neutralizes the pH, prevents osmotic swelling by CQ/Mon, and was shown to block LC3 lipidation (Florey et al., 2015, Jacquin et al., 2017). When BafA1 was added simultaneously, CQ was found to induce LC3 despite the presence of BafA1 (Mauthe et al., 2018), and Mon was shown to still be able to break endosomal membranes and recruit LC3 to EEA1-positive endosomes (Fraser et al., 2019). However, CQ-induced LC3 recruitment to latex bead-containing phagosomes or entotic vacuoles, i.e. LAP-like autophagy, was blocked (Florey et al., 2015). Consistent with this literature, we found increased LC3B lipidation already within 30 min of CQ treatment independently of BafA1 (no preincubation).
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Upon longer incubations, LC3B lipidation is very strong already with BafA1 alone so that the effect of CQ cannot be assessed anymore, since both drugs inhibit autophagic flux.
Furthermore, we found a CQ-dependent increase in WIPI2- and LC3B-positive puncta to be insensitive to BafA1 (panel A below). Colocalization of Rabaptin5 to LC3B and LC3B to Rabaptin5 significantly increased upon CQ treatment independently of the presence of BafA1 (no pretreatment), indicating that at least a large part of CQ-induced LC3B puncta is not due to LAP-like autophagy.
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Minor concerns Both for Figure 2 and Supplementary Figure 7 it will be clearer to have the images in colour rather than black and white for better interpretation.
We thought the grayscale images were clearer, but are happy to provide color images.
The interaction of FIP200 and ATG16L1 with Rabaptin5 is well characterized with immunoprecipitation and imaging but the interaction of Rabaptin5 in presence of chloroquine with FIP200 and ATG16L1 DWD are missing and it will be important to include if in the presence of chloroquine these interactions will increase or not.
We can do co-IP experiments also upon CQ treatment.
In order to further support the role of Rabaptin5 for LC3 lipidation upon chloroquine induced membrane damage, western blots of WT, +Rabaptin5, Rabaptin5 KO, Rabaption5 KO +WT or +AAA cell lines were analysed. However, the lysates were collected upon 30 minutes of chloroquine treatment which does not correlate with the imaging performed in Figure 2 as the number of LC3 vesicles did not show an increase upon 30 minutes of chloroquine treatment. The authors should include the 150 minutes time point for the LC3 lipidation in these conditions.
Because CQ inhibits autophagic flux, LC3-II accumulates after longer times in all cell lines. The differences can only be seen early.
The experiments with Salmonella are of great quality. The relationship of Rabaptin5 with SCV and the endomembrane damage induced by Salmonella could be further elucidated with Rabaptin5 positive vesicles at early infection stages. It is not very clear from the text how authors link the endosomal network previously described for chloroquine with infection. It would be important here to show that Salmonella mutants unable to damage endosomal membranes do not have an effect. In Figure 7 panel C, the time points on graphs are in hours but it should be in minutes. corrected.
Since Salmonella require T3SS for infection of HEK cells and T3SS causes the membrane damage, the proposed experiment is difficult.
The events of targeting the damaged membranes for degradation was well characterized by the recognition of these membranes by Gal3, Gal8 and recruitment of autophagic receptors to the site of damage (Chauhan et al. 2016; Jia et al. 2019; Thurston et al. 2012; Maejima et al. 2013; Kreibich et al. 2015). This manuscript introduces a new potential platform for the formation of autophagic machinery on endosomes with the interaction of Rabaptin5 with FIP200 and ATG16L1, however more evidence is required to link this to the clearance of damaged membranes. Previously it was shown that endolysosomal compartments that were neutralized and swollen by monensin and chloroquine had been directed to degradation by direct conjugation of LC3 to single membranes via noncanonical autophagy, but here authors propose another mechanism for this event via canonical autophagy.
As discussed in the general response above, the literature reports CQ and Mon to initiate both canonical autophagy and LAP-like autophagy, the latter particularly on phagosomes containing latex beads or entotic vacuoles. Our results – including the additional data above –concern the effects of CQ and Mon damaging early endosomes and causing recruitment of galectins and ubiquitination, triggering autophagy dependent on the ULK complex and WIPI2 as hallmarks of canonical autophagy, and Rabaptin5. The reviewer comments highlighted the possibility of LAP-like autophagy occurring in parallel, perhaps on endosomes that are not broken, which might explain the relative insensitivity of LC3 puncta induced by CQ and Mon – compared to the strong and robust reduction of WIPI2 puncta – on the knockdown of FIP200, ATG13, or Rabaptin5. In an alternative explanation, inhibition of autophagic flux causes remaining canonical autophagy to accumulate, while WIPI2 puncta are strongly inhibited. In support of the latter interpretation, ULK inhibition by MRT68921 (Fig. 4C and D) or FIP200 knockout (Fig. 6B and C) abolished CQ-induced LC3 structures, suggesting that – unlike on phagosomes or entotic vacuoles – there is little LAP-like autophagy. We propose to revise the manuscript to discuss these considerations more clearly.
Reviewer #1 (Significance (Required)):
Overall this work is very novel and shows some evidence of early endosomal autophagy. It could be relevant for some for of receptor-mediated signalling (although it is not discussed by the authors) My experience is in intracellular trafficking of pathogens and membrane damage.
**Referee Cross-commenting**
In my opinion, the only way you can distinguish between double or single membrane is by EM. For me, the important part is to show this is targeting of early endosomes to autophagy, either using other early endosomal markers, analysing by WB some early endosome receptors such as TfR or other inhibitors. If the authors are able to address some these comments, I agree the paper will be in a better position for publication.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Millarte et al study the role of Radaptin-5 (Rbpt5) during early endosome damage recognition by autophagy. The authors focus on using chloroquine (CQ) as an agent to induce endosomal swelling/damage and suggest that Rbpt5 is required for the recruitment of the autophagy machinery to perturbed endosomes. They further use salmonella infection as a model to confirm the role of Rbpt5 in this process. The authors initially show that Rbpt5 binds to FIP200 and subsequently focus on its interaction with ATG16L1 and identify a mutant that is unable to bind ATG16L1 or mediate the recognition of early endosomes by autophagy. Overall, this is an interesting study which provides molecular insights of how early endosomes can be targeted by the autophagy machinery where Rbpt5 may act as an autophagy receptor. Some specific comments are as follows:
Fig.3A: siRbpt5 seems to induce the localization of LC3 to ring-like structures during CQ treatment. Are these LAP-like structures (e.g. sensitive to BafA1 treatment)? And were they included in the quantification in Fig.3C?
Ring-like LC3 structures were also counted.
As discussed in the general remarks above, it is a possibility that knockdown-resistent LC3 recruitment (particularly rings) is due to a CQ-induced LAP-like process. The alternative explanation is that there is residual canonical autophagy upon knockdown of Rabaptin5, ATG13, or FIP200: while WIPI2 puncta are strongly reduced, LC3-positive structures accumulate due to inhibition of autophagic flux. In support of the latter interpretation, ULK inhibition by MRT68921 (Fig. 4C and D) or FIP200 knockout (Fig. 6B and C) abolished CQ-induced LC3 puncta or rings.
We can also test BafA1 treatment. Certainly, we will revise the text to discuss this point in more detail.
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Fig.4A&B: Since Rbpt5 KD has a weak effect on LC3 puncta formation (Fig.3) and to distinguish the effects of CQ in inducing LAP, the effects of ATG13 and ULK1 KD should be assessed by localising Rbpt5 with WIPI2 or ATG16L1.
We can do that.
Fig.4: It is not clear why ULK1 KD would affect Torin1-induced autophagy but not LC3/WIPI2 localisation during CQ induced early endosome-damage. As the ULK inhibitors can target other pathways, the authors should confirm this finding in ULK1/2 double KO or KD cells.
We have used **MRT68921, because it is frequently used in the literature for this purpose with high specificity. It was used for example by Lystad et al. (2019) together with VPS34IN1 to block all canonical autophagy to analyze exclusively noncanonical effects of monensin treatment. We could perform ULK1/2 double knockdowns, but since ULK2 cannot be detected on immunoblots in HEK293 cells, the result would be interpretable only when there is an effect.
Fig.5: The contribution of FIP200 in the interaction between Rbpt5 and ATG16L1 is unclear. Is binding between Rbpt5 and ATG16L1 mediated by ATG16L1's interaction with FIP200? The plasmid details describing the delta-WD40 deletion plasmid used in this study are missing and could be important to confirm that the detla-WD40 still retains binding to FIP200.
We will of course include the details on the deletion plasmid, which were missing by mistake. Our WD deletion construct of ATG16L1 consists of residues 1–319, precisely deleting just the WD40 repeats, but retaining the FIP200 interaction sequence and the second membrane binding segment (b).
We did a co-immunoprecipitation experiment and found both wild-type ATG16L1 and the ∆WD mutant to co-immunoprecipitate with FIP200:
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Fig.5E: the authors should test Rbpt5 AAA mutant binding to FIP200. Since the mutant appears to express less, its binding to ATG16L1 should be quantified or repeated with more comparable expression levels.
We will quantify the immunoblots and perhaps attempt getting more equal expression levels.
Fig.6: CQ treatment can induce various endosomal damage (in addition to early endosomes) and LC3 lipidation processes (e.g. LAP-like). The authors show that Rbpt5 is specifically involved in damaged early endosome autophagy. In this figure, it would be important to distinguish CQ-induced LC3 puncta as a result of early endosome damage or other lipidation processes (e.g. canonical or non-canonical autophagy). The use of FIP200 KO cells shows that LC3 puncta is inhibited. However, here a specific readout to look at early endosome recognition by autophagy is important. The authors can localize early endosome markers (EEA1) with autophagy players (e.g. WIPI2 and LC3). This is also relevant to other figures (e.g. supplementary figure 7E).
Rabaptin5 is a bona fide marker of Rab5-positive early sorting endosomes. As a control, we confirmed colocalization of Rabaptin5 with transferrin receptor, another endosomal marker, on CQ-induced rings (Fig. 2B). We also analyzed swollen endosomes with triple-staining for Rabaptin5/ transferrin receptor/ Gal3 as shown in this gallery (30 min CQ, as in Fig. 2). All Rabaptin5-positive swollen endosomes (rings) were positive for transferrin receptor and ~80% for mCherry-Gal3.
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Our results are in agreement with Fraser et al. (2019) where they use EEA1 as an endosomal marker upon monensin treatment.
We also performed a colocalization analysis for Rabaptin5 and LC3B, showing enhanced colocalization after CQ treatment for 150 min: ~20% of LC3B is (still) pos for Rabaptin5 after 150 min of CQ treatment:
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Fig.6F&G: the authors should show representative images of these localization images quantified here. These can be added in the supplementary figures.
We are happy to do this.
**Minor comments:**
Fig.2E: FIP200 seems to be highly overexpressed in this image. Commercial antibodies that recognise endogenous FIP200 are widely used and should be tested to confirm the colocalisation between FIP200 and Rbpt5.
We plan to do this.
Fig.7C image: the different setting denoted by +/-, +/+ ..etc are not clearly defined.
We will improve this.
Reviewer #2 (Significance (Required)):
This is a interesting study and provides important mechanistic insights underlying the recognition of perturbed early endosomes by the autophagy machinery. Researchers interested in endosomal trafficking or autophagic substrate recognition are likely to benefit from this study.
**Referee Cross-commenting**
In my opinion, the authors have attempted to distinguish single membrane from double membrane LC3 lipidation by looking at the ULK complex requirement. As other reviewers suggested, this can be further confirmed by using ATG16L1 mutants. It is important however that these experiments are supplemented by co-localising autophagy proteins with alternative early endosome markers when Rbpt5 is inhibited.
I think if the authors are able to address the suggested experiments, this would help improve the manuscript and make it suitable for publication.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
Millarte and colleagues find that Rabaptin5, a critical regulator of Rab5 activity, and a protein localized to early endosomes, interacts with FIP200 and ATG16L1. This interaction is confirmed and validated by a number of approaches (yeast 2 H, co-immunoprecipitation) and the binding sites of Rabaptin5 are mapped on FIP200 and ATG16L1. More precisely the binding site for ATG16L1 is nicely mapped on Rabaptin 5 by analogy with other ATG16L1 binders. The authors investigate the significance of this binding of Rabaptin5 to the autophagy proteins by proposing this interaction is required for targeting "autophagy to damaged endosomes". Endosomes are damaged with short treatments of chloroquine, a well studied compound previously shown to inhibit autophagy by disrupting fusion of autophagosomes with lysosomes. They propose the recruitment of autophagy (proteins) to the damaged endosomes may allow them to be eliminated. They use another model (phagocytosis of salmonella) to probe the role for rabaptin5 and its partners FIP200 and ATG16L1 in the well-documented role of autophagy on the elimination of salmonella in SCVs (Salmonella containing vacuole) formed from endosomes. Using short infection time points, and the Rabaptin5 mutants which prevent ATG16L1 binding they suggest Rabaptin5 binding contributes to elimination and killing of Salmonella by recruitment of ATG16L1.
**Major comments:**
- The authors make an unfortunate and confusing choice of wording in the title and the text of "autophagy being recruited" to damaged early endosomes. A protein can recruit another protein but it can not recruit a process or pathway to a membrane.
In the title we use the term "target". It is OK for us to avoid the expression "recruiting autophagy".
The authors conclude that Rabaptin5 may have a role in autophagy directed to damaged early endosomes. The conclusion that Rabaptin5 binds FIP200 and ATG16L1 are convincing. The main issue is however in identifying what sort of process they are following. They have shown WIPI2 and LC3 can be recruited to early endosomes after 30 min chloroquine treatment but there is no data to explain the consequences of the binding of these proteins. They do not provide proof that canonical autophagosomes are formed which engulf and remove the damaged endosomes, nor do they show that the recruitment of WIPI2 is to a single membrane (presumably damaged early endosomes) which would be a non-canonical pathway. They often use the terminology "chloroquine-induced autophagy" (see Figure 4) but have virtually no proof they have induced either canonical or non-canonical pathways in their experiments. The only evidence they provide that there is some alteration in a membrane-mediated event is increase in lipidation of LC3 in Figure 6. The authors must follow either an early endosome protein or cargo to demonstrate lysosome-mediated degradation indicative of autophagy, or demonstrate the process is a variation on non-canonical autophagy.
We analyzed transferrin receptor levels with and without CQ to test degradation of an early endosomal marker protein. Since CQ inhibits autophagic flux, this assay may not be very sensitive. Nevertheless, we found a significant reduction of ~15% and ~30% after overnight incubation with CQ in parental HEK293 cells and in Rbpt5-KO cells re-expressing wild-type Rabaptin5, resp., but no reduction in Rbpt5-KO cells expressing the Rabaptin5-AAA mutant defective in binding to ATG16L1:
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There are concerns about the replicates done for many experiments in particular the co-immunoprecipitations which are not quantified (Figure 1 and 5).
We will quantify these blots.
The rescue experiments, even if done with stable cells lines made in the parental HEK293 cell line should be viewed with caution because of the very different amounts of Rabaptin5 (see Figure 6A). The overexpression of Rabaptin5 has not been well studied and comparisons with the mutants are therefore preliminary (Figure 6F and G).
Fig 6A shows that Rabaptin5 levels are similar except for +Rbpt, where they are higher, and R-KO, which has none. Additional Rabaptin5 seems not to significantly enhance early WIPI and ATG16L1 colocalization.
Conclusions about the role of the ULK complex, or ULK1 versus ULK2, should be expanded by studying the activity of the complex (phosphorylation of ATG13 for example) in order to make the conclusions more significant.
We consider this to be beyond the scope of this study. Rabaptin5-dependent autophagy depends on the components of the ULK complex.
**Minor comments:**
- Much of the labelling in the immunofluorescence images is not visible even on the screen version.
We were careful to have the signals within the dynamic range of the image, but we can enhance the signals for better visibility.
The LC3-lipidation experiment (Figure 6D) should be re-analysed by normalization to the loading control. The result may be significantly different and is open to re-interpretation. The quality of this western blot is also very poor.
Quantitation was based on the ratio between LC3B-I and -II or the **percentage of II of the total, always within the same lane and therefore largely independent of loading.
Reviewer #3 (Significance (Required)):
This manuscript topic fits into the field of study of canonical versus non-canonical autophagy. This literature is best described as "LAP" first discovered by Doug Green, (Sanjuan in 2009) but more recently as a phenomena induced by monesin, and viral infection amongst others. Most relevant to this study are the references (in the text) by Florey (Autophagy 2015), Fletcher (EMBO J, 2018) and others. However, this manuscript fails to cite and consider the critical findings in a key study published by Lystad et al., Nature Cell Biology 2019, which examines the role of ATG16 in both canonical and non-canonical autophagy. The current study if placed into the context of the Lystad study would have significantly more value, and potentially make the findings more significant.
We did not refer to Lystad et al. (2019), because they analyzed different ATG16L1 mutants on their contribution to monensin-induced processes on LC3 lipidation after completely blocking canonical autophagy with the ULK inhibitor MRT68921 and the VPS34 inhibitor VPS34IN1. The Rabaptin5-dependent CQ-induced processes are blocked by MRT68921 (Fig. 4C). We plan to refer to this study in the revision.
Furthermore, the short chloroquine treatments used here could be of interest to the field if using the cited study of Mauthe et al., (which very clearly defines the effect of chloroquine after long (5 hrs treatment)) the authors would to revisit and repeat some of the key experiments in order to demonstrate the effects of 30 minute treatment. Does such short treatment block fusion? Does it affect the pH of the acidic compartments? Does it inactivate the endocytitic pathway? As the manuscript stands the lack of this understanding of the effect of chloroquine at short times, makes the observations difficult to be place into any biological context.
This reviewer has expertise in autophagy, autophagosome formation and is familiar with the areas of endocytosis and infection.
**Referee Cross-commenting**
I think a major concern about the manuscript which is present in all reviews is the lack of clarity about what type of membrane LC3 is added to- is this the damaged endosome or a forming autophagosome? This leads to the question of what type of process is being observed here? non-canonical versus canonical autophagy.
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Referee #3
Evidence, reproducibility and clarity
Millarte and colleagues find that Rabaptin5, a critical regulator of Rab5 activity, and a protein localized to early endosomes, interacts with FIP200 and ATG16L1. This interaction is confirmed and validated by a number of approaches (yeast 2 H, co-immunoprecipitation) and the binding sites of Rabaptin5 are mapped on FIP200 and ATG16L1. More precisely the binding site for ATG16L1 is nicely mapped on Rabaptin 5 by analogy with other ATG16L1 binders. The authors investigate the significance of this binding of Rabaptin5 to the autophagy proteins by proposing this interaction is required for targeting "autophagy to damaged endosomes". Endosomes are damaged with short treatments of chloroquine, a well studied compound previously shown to inhibit autophagy by disrupting fusion of autophagosomes with lysosomes. They propose the recruitment of autophagy (proteins) to the damaged endosomes may allow them to be eliminated. They use another model (phagocytosis of salmonella) to probe the role for rabaptin5 and its partners FIP200 and ATG16L1 in the well-documented role of autophagy on the elimination of salmonella in SCVs (Salmonella containing vacuole) formed from endosomes. Using short infection time points, and the Rabaptin5 mutants which prevent ATG16L1 binding they suggest Rabaptin5 binding contributes to elimination and killing of Salmonella by recruitment of ATG16L1.
Major comments:
- The authors make an unfortunate and confusing choice of wording in the title and the text of "autophagy being recruited" to damaged early endosomes. A protein can recruit another protein but it can not recruit a process or pathway to a membrane.
- The authors conclude that Rabaptin5 may have a role in autophagy directed to damaged early endosomes. The conclusion that Rabaptin5 binds FIP200 and ATG16L1 are convincing. The main issue is however in identifying what sort of process they are following. They have shown WIPI2 and LC3 can be recruited to early endosomes after 30 min chloroquine treatment but there is no data to explain the consequences of the binding of these proteins. They do not provide proof that canonical autophagosomes are formed which engulf and remove the damaged endosomes, nor do they show that the recruitment of WIPI2 is to a single membrane (presumably damaged early endosomes) which would be a non-canonical pathway. They often use the terminology "chloroquine-induced autophagy" (see Figure 4) but have virtually no proof they have induced either canonical or non-canonical pathways in their experiments. The only evidence they provide that there is some alteration in a membrane-mediated event is increase in lipidation of LC3 in Figure 6. The authors must follow either an early endosome protein or cargo to demonstrate lysosome-mediated degradation indicative of autophagy, or demonstrate the process is a variation on non-canonical autophagy.
- There are concerns about the replicates done for many experiments in particular the co-immunoprecipitations which are not quantified (Figure 1 and 5).
- The rescue experiments, even if done with stable cells lines made in the parental HEK293 cell line should be viewed with caution because of the very different amounts of Rabaptin5 (see Figure 6A). The overexpression of Rabaptin5 has not been well studied and comparisons with the mutants are therefore preliminary (Figure 6F and G).
- Conclusions about the role of the ULK complex, or ULK1 versus ULK2, should be expanded by studying the activity of the complex (phosphorylation of ATG13 for example) in order to make the conclusions more significant.
Minor comments:
- Much of the labelling in the immunofluorescence images is not visible even on the screen version.
- The LC3-lipidation experiment (Figure 6D) should be re-analysed by normalization to the loading control. The result may be significantly different and is open to re-interpretation. The quality of this western blot is also very poor.
Significance
This manuscript topic fits into the field of study of canonical versus non-canonical autophagy. This literature is best described as "LAP" first discovered by Doug Green, (Sanjuan in 2009) but more recently as a phenomena induced by monesin, and viral infection amongst others. Most relevant to this study are the references (in the text) by Florey (Autophagy 2015), Fletcher (EMBO J, 2018) and others. However, this manuscript fails to cite and consider the critical findings in a key study published by Lystad et al., Nature Cell Biology 2019, which examines the role of ATG16 in both canonical and non-canonical autophagy. The current study if placed into the context of the Lystad study would have significantly more value, and potentially make the findings more significant.
Furthermore, the short chloroquine treatments used here could be of interest to the field if using the cited study of Mauthe et al., (which very clearly defines the effect of chloroquine after long (5 hrs treatment)) the authors would to revisit and repeat some of the key experiments in order to demonstrate the effects of 30 minute treatment. Does such short treatment block fusion? Does it affect the pH of the acidic compartments? Does it inactivate the endocytitic pathway? As the manuscript stands the lack of this understanding of the effect of chloroquine at short times, makes the observations difficult to be place into any biological context.
This reviewer has expertise in autophagy, autophagosome formation and is familiar with the areas of endocytosis and infection.
Referee Cross-commenting
I think a major concern about the manuscript which is present in all reviews is the lack of clarity about what type of membrane LC3 is added to- is this the damaged endosome or a forming autophagosome? This leads to the question of what type of process is being observed here? non-canonical versus canonical autophagy.
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Referee #2
Evidence, reproducibility and clarity
Millarte et al study the role of Radaptin-5 (Rbpt5) during early endosome damage recognition by autophagy. The authors focus on using chloroquine (CQ) as an agent to induce endosomal swelling/damage and suggest that Rbpt5 is required for the recruitment of the autophagy machinery to perturbed endosomes. They further use salmonella infection as a model to confirm the role of Rbpt5 in this process. The authors initially show that Rbpt5 binds to FIP200 and subsequently focus on its interaction with ATG16L1 and identify a mutant that is unable to bind ATG16L1 or mediate the recognition of early endosomes by autophagy. Overall, this is an interesting study which provides molecular insights of how early endosomes can be targeted by the autophagy machinery where Rbpt5 may act as an autophagy receptor. Some specific comments are as follows:
Fig.3A: siRbpt5 seems to induce the localization of LC3 to ring-like structures during CQ treatment. Are these LAP-like structures (e.g. sensitive to BafA1 treatment)? And were they included in the quantification in Fig.3C?
Fig.4A&B: Since Rbpt5 KD has a weak effect on LC3 puncta formation (Fig.3) and to distinguish the effects of CQ in inducing LAP, the effects of ATG13 and ULK1 KD should be assessed by localising Rbpt5 with WIPI2 or ATG16L1.
Fig.4: It is not clear why ULK1 KD would affect Torin1-induced autophagy but not LC3/WIPI2 localisation during CQ induced early endosome-damage. As the ULK inhibitors can target other pathways, the authors should confirm this finding in ULK1/2 double KO or KD cells.
Fig.5: The contribution of FIP200 in the interaction between Rbpt5 and ATG16L1 is unclear. Is binding between Rbpt5 and ATG16L1 mediated by ATG16L1's interaction with FIP200? The plasmid details describing the delta-WD40 deletion plasmid used in this study are missing and could be important to confirm that the detla-WD40 still retains binding to FIP200.
Fig.5E: the authors should test Rbpt5 AAA mutant binding to FIP200. Since the mutant appears to express less, its binding to ATG16L1 should be quantified or repeated with more comparable expression levels.
Fig.6: CQ treatment can induce various endosomal damage (in addition to early endosomes) and LC3 lipidation processes (e.g. LAP-like). The authors show that Rbpt5 is specifically involved in damaged early endosome autophagy. In this figure, it would be important to distinguish CQ-induced LC3 puncta as a result of early endosome damage or other lipidation processes (e.g. canonical or non-canonical autophagy). The use of FIP200 KO cells shows that LC3 puncta is inhibited. However, here a specific readout to look at early endosome recognition by autophagy is important. The authors can localize early endosome markers (EEA1) with autophagy players (e.g. WIPI2 and LC3). This is also relevant to other figures (e.g. supplementary figure 7E).
Fig.6F&G: the authors should show representative images of these localization images quantified here. These can be added in the supplementary figures.
Minor comments:
Fig.2E: FIP200 seems to be highly overexpressed in this image. Commercial antibodies that recognise endogenous FIP200 are widely used and should be tested to confirm the colocalisation between FIP200 and Rbpt5.
Fig.7C image: the different setting denoted by +/-, +/+ ..etc are not clearly defined.
Significance
This is a interesting study and provides important mechanistic insights underlying the recognition of perturbed early endosomes by the autophagy machinery. Researchers interested in endosomal trafficking or autophagic substrate recognition are likely to benefit from this study.
Referee Cross-commenting
In my opinion, the authors have attempted to distinguish single membrane from double membrane LC3 lipidation by looking at the ULK complex requirement. As other reviewers suggested, this can be further confirmed by using ATG16L1 mutants. It is important however that these experiments are supplemented by co-localising autophagy proteins with alternative early endosome markers when Rbpt5 is inhibited.
I think if the authors are able to address the suggested experiments, this would help improve the manuscript and make it suitable for publication.
Referee Cross-commenting
In my opinion, the authors have attempted to distinguish single membrane from double membrane LC3 lipidation by looking at the ULK complex requirement. As other reviewers suggested, this can be further confirmed by using ATG16L1 mutants. It is important however that these experiments are supplemented by co-localising autophagy proteins with alternative early endosome markers when Rbpt5 is inhibited.
I think if the authors are able to address the suggested experiments, this would help improve the manuscript and make it suitable for publication.
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Referee #1
Evidence, reproducibility and clarity
In the current manuscript, Millarte et al reports a novel role of Rabaptin5 in selectively clearing damaged endosomes via canonical autophagy. They have identified FIP200 as a novel interactor of Rabaptin5 under basal conditions using yeast-two hybrid screening and further confirmed the interaction of Rabaptin5 with FIP200 with immunoprecipitation. They next used Chloroquine and monitored colocalization of the Rabaptin5 with WIPI2, ATG16L1 and LC3B to demonstrate the potential interaction of Rabaptin5 with the autophagic machinery. They have primarily used Gal-3 as a marker of membrane damage after 30 minutes of Chloroquine treatment. In order to further elucidate the role of Rabaptin5 in autophagic induction mediated by Chloroquine, they have silenced Rabaptin5, FIP200, ULK1 and ATG13 and observed a decrease in the number of LC3 or WIPI2 autophagosome formation. Based on these observations they tested if Rabaptin5 interacts with ATG16L1 upon Chloroquine treatment and confirmed their interaction with potential interaction sites of both Rabaptin5 with ATG16L1 with IP. The authors confirmed the interaction of Rabaptin5 with ATG16L1 by complementing the KO line with the mutant form of Rabaptin5 containing alanine residues in its consensus motif. Finally, they have used Salmonella and SCV as a model to study the role of Rabaptin5 in endomembrane damage and monitored a 50% decrease in the removal of Salmonella in Rabaptin5 KO or KD cells.
Major concerns One of the major concerns is the membrane damage reported by chloroquine which is known to induce lysosomal swelling and further targeting of the swollen compartments to degradation by direct conjugation of LC3 onto single membrane as a form of non-canonical autophagy. The evidence regarding membrane damage by Gal3 colocalization on the Rabaptin5 vesicles is preliminary. As suggested by the authors the canonical autophagy pathway recognizing damaged membranes recruits also ALIX to the damaged membrane which was not observed in Supplementary Figure 2. The link to membrane damage by chloroquine and monensin with Rabaptin5 is not convincing as there is not sufficient evidence of membrane damage. In relation to this issue authors should consider using other damage markers as Gal8, p62 or NDP52 to provide additional claim with respect to membrane damage induced by chloroquine.
One of the main claims here is that Rabaptin5 regulates the targeting of damaged endosomes to autophagy. Clearly, these are early endosomes as stated in the abstract. However, the evidence presented here showing these are early endosomes is not convincing. Analysing Gal3 and Gal8 positive vesicles that are Rabaptin5 positive and an early endosomal marker will be important in this context. For example, there need to be additional evidence showing that early endosomes are targeted to autophagy. Is the degradation of TfR affected by this targeting? Did the authors look at the effect of Bafilomycin A1? If this process affects exclusively early endosomes, it should be BafA1 independent. This will direct more into the cellular function of this process.
Minor concerns Both for Figure 2 and Supplementary Figure 7 it will be clearer to have the images in colour rather than black and white for better interpretation.
The interaction of FIP200 and ATG16L1 with Rabaptin5 is well characterized with immunoprecipitation and imaging but the interaction of Rabaptin5 in presence of chloroquine with FIP200 and ATG16L1 WD are missing and it will be important to include if in the presence of chloroquine these interactions will increase or not.
In order to further support the role of Rabaptin5 for LC3 lipidation upon chloroquine induced membrane damage, western blots of WT, +Rabaptin5, Rabaptin5 KO, Rabaption5 KO +WT or +AAA cell lines were analysed. However, the lysates were collected upon 30 minutes of chloroquine treatment which does not correlate with the imaging performed in Figure 2 as the number of LC3 vesicles did not show an increase upon 30 minutes of chloroquine treatment. The authors should include the 150 minutes time point for the LC3 lipidation in these conditions.
The experiments with Salmonella are of great quality. The relationship of Rabaptin5 with SCV and the endomembrane damage induced by Salmonella could be further elucidated with Rabaptin5 positive vesicles at early infection stages. It is not very clear from the text how authors link the endosomal network previously described for chloroquine with infection. It would be important here to show that Salmonella mutants unable to damage endosomal membranes do not have an effect. In Figure 7 panel C, the time points on graphs are in hours but it should be in minutes.
The events of targeting the damaged membranes for degradation was well characterized by the recognition of these membranes by Gal3, Gal8 and recruitment of autophagic receptors to the site of damage (Chauhan et al. 2016; Jia et al. 2019; Thurston et al. 2012; Maejima et al. 2013; Kreibich et al. 2015). This manuscript introduces a new potential platform for the formation of autophagic machinery on endosomes with the interaction of Rabaptin5 with FIP200 and ATG16L1, however more evidence is required to link this to the clearance of damaged membranes. Previously it was shown that endolysosomal compartments that were neutralized and swollen by monensin and chloroquine had been directed to degradation by direct conjugation of LC3 to single membranes via noncanonical autophagy, but here authors propose another mechanism for this event via canonical autophagy.
Significance
Overall this work is very novel and shows some evidence of early endosomal autophagy. It could be relevant for some for of receptor-mediated signalling (although it is not discussed by the authors) My experience is in intracellular trafficking of pathogens and membrane damage.
Referee Cross-commenting
In my opinion, the only way you can distinguish between double or single membrane is by EM. For me, the important part is to show this is targeting of early endosomes to autophagy, either using other early endosomal markers, analysing by WB some early endosome receptors such as TfR or other inhibitors. If the authors are able to address some these comments, I agree the paper will be in a better position for publication.
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Reply to the reviewers
We would like to thank our reviewers for their critical reading and constructive comments. We have addressed all of their points and have included below a detailed reference to the changes we made accordingly. We have also added an additional supplemental figure.
Reviewer #1 :
**Major comments:**
- The authors highlight in their conclusion that the new Python library has the potential to accelerate and expand microscopy development. I agree with this statement since classes and methods do not need to be written in Python from scratch anymore. However, I would recommend that the authors include in their conclusion the value of the library for reproducibility if the final python acquisition code is shared along with publications. Nowadays, scientists frequently write in their publications that LabView or a specific commercial scope's acquisition software was used without any acquisition code. Python-Microscope would have the potential to change this trend, and the authors need to stress this aspect and its value for reproducibility in science accordingly. This is a good point. We have added the following to the discussion section.
“A further advantage of the approach provided by Microscope is in increasing reproducibility in science. Scientists frequently write in their publications that LabView or a specific commercial scope's acquisition software was used without any specific acquisition settings, code or macros to assist with reproduction. This is especially critical in complex experimental setups where specifics of acquisition are particularly important. Microscope has the potential to change this trend, allowing authors to freely publish simple code demonstrating exactly how their control and acquisition operates. Additionally, the defined device interfaces allow such code to be ported to other specific hardware with minimal changes.”
The authors need to provide a more comprehensive overview of the currently used data acquisition strategies in their introduction. Currently, they highlight the acquisition software provided by vendors for data acquisition (mainly used by life scientists and not necessary scope builders/developers), Micro-Manager (mainly used by life scientists; currently also restricted to wide-field systems), and LabView (for advanced microscope systems; used by advanced developers).
However, most advanced microscope builders use MatLab (Chmyrov et al. Nature Methods (2013) - https://doi.org/10.1038/nmeth.2556, Ta et al. Nature Communications (2015) - https://doi.org/10.1038/ncomms8977 , etc.), Python (York et al. Nature Methods (2013) - https://doi.org/10.1038/nmeth.2687, etc.), and LabView to write their acquisition software. Since the manuscript focused on advanced microscopes, the authors need to position their library with respect to Matlab and Python's current use as well.
We thank the reviewer for pointing out the omission of Matlab control solutions and extending the references to other Python based approaches. We have also added a reference to the Pycro-Manager framework for Micro-Manager which has been published since our original submission.
We have added Matlab to the LabVIEW generalised control software section which now reads:
“custom control software often in LabVIEW or Matlab, both proprietary software. LabVIEW offers a visual programming environment that is commonly used for building instruments in the physical sciences, whereas Matlab is a programming platform with a focus on numeric computing.”
And extended the description sections in the introduction with the following paragraphs and references:
“Matlab is a numerical focused programming environment that scientists are often familiar with for data processing. It has frequently been used for microscopy, leveraging a number of available Matlab sub packages to provide GUI’s and easy access to complex data processing steps. The use of Matlab for microscope control is common in the field but the actual code is rarely shared and often custom to a single microscope setup and associated to image reconstruction (Chmyrov et al., 2013, Ta et al., 2015). Exceptions are ScanImage for the control of laser scanning microscopes (Pologruto et al., 2003), and Matlab Instrument Control (MIC) for the control of individual microscope components (Pallikkuth et al., 2018). Matlab provides a textual programming language simplifying code sharing and version control, however, Matlab is proprietary closed source software and the general requirement of many extensions significantly adds to the cost of implementing many systems.”
“There is currently an increasing number of software options for microscope control in Python, many of which are in the form of custom scripts specific to a microscope (Alvelid and Testa, 2019, York et al., 2013) but some provide a fully integrated microscope control environments, namely PYME https://www.python-microscopy.org/ for SMLM and ACQ4 (Campagnola et al., 2014) for electrophysiology. While this code is freely available and can be modified, their design around a specific setup, technique, or environment reduces its potential for code reuse in other projects.”
The authors need to give (a) software provided by vendors, (b) LabView, and (c) Micro-Manager, more credit.
(a) Several microscope vendors (e.g., Abberior Instruments - https://imspectordocs.readthedocs.io/en/latest/specpy.html ) allow their scopes can be externally controlled to enable the execution of customer-driven acquisition strategies which the vendor's acquisition software itself might not have implemented with. The authors might want to include that scope vendors aim for more customer modifiable acquisition software.
The reviewer makes a good point, especially in the fact that a number of microscope vendors provide Python interfaces for their systems. We have added the following text:
Several microscope vendors, such as Abberior Instruments and Zeiss, provide Python interfaces to enable instrument control from Python. These are all very useful additions to proprietary systems, however they have a fundamental draw back that each manufacture produces their own abstractions meaning code from one system is not compatible with another. Although these interfaces leverage the substantial Python infrastructure they are not generalisable and hence fail to enhance portability or reproducibility.
The fact that these companies are providing Python interfaces to their instruments indicates the general interest of the community in Python as a programming language to extend hardware capabilities. This demonstrates the potential benefit of an entirely Python based interface to a wide range of hardware.
(b) The authors criticize that LabView code can be hard to understand, reproduce and maintain. However, similar to writing good code in general, there are best practice strategies for writing good LabView code to ensure scalability, readability, and maintainability available as well (https://learn.ni.com/learning-paths/labview-core-3-2016-english ). The primary problem might lie more on the side of lousy coding practice than on LabView's side to perform appropriately.
This is a fair point and we have revised the manuscript as indicated below. However, it remains true that it is much harder for a non-expert to write high quality code in LabView than in Python. This is particularly evident in complex systems.
We have changed the section about LabView to read:
“The visual nature of the programming environment makes simple projects easy but systems with a large number of hardware components or complicated control architecture can become hard to understand, reproduce, and maintain. Although this complication can be reduced with good programming practices, it is not uncommon to outsource such work to a commercial company \citep{chhetri2020software} because good code writing in LabView is significantly more challenging than in popular general purpose languages such as Python. Additionally, the LabView work flow does not integrate well into modern distributed source control infrastructure such as mercurial or git, a necessity for modern open source development.”
(c) The authors should include the current effort by Pinkard et al. (Pinkard et al. Nature Methods (2021) - https://doi.org/10.1038/s41592-021-01087-6 ) in their discussion.
A pre-print version of this paper was available on arXiv and cited in our original submission. Now this paper is published we have included the published reference and the following text has been added to our discussion section.
“As mentioned in the introduction, micromanager has a recently introduced Python interface, Pycro-Manager (Pinkard et al. 2021). This simplifies connections between micromanager based hardware interfaces and Python based analysis and control. Although this reduces the effort in using Python for control and online analysis compared to other approaches it does not provide direct access to the hardware via Python. This interface keeps the existing micromanager infrastructure. Particularly new hardware interfaces still need code in both C/C++ and Java before they are accessible via the Python interface.”
The authors might want to explain how they plan to facilitate the library's adoption and the long-term maintenance within the microscopy community. Do they plan to create a new category on Image.sc, which would allow the community to interact with the developers? etc. Furthermore, who will keep writing wrappers to the libraries provided by the vendors? etc
This is a critical point, as the reviewer states, community involvement is essential to continuation of the project and provide a useful tool going forward. We have already published several systems utilising this software platform and are working hard to expand its user base. We have asked for people to post question on the image.sc forums (https://image.sc/) and we also interact with developers and users on the github issue pages (https://github.com/python-microscope/microscope/issues). We have recently implemented a fully automated microscope on a simple motorized stand from Zaber. This provides a fully automated microscopy solution for a very low cost.
We have edited the end of the discussion to read
Microscope is a free and open source project currently being used in several labs with an open development approach. Our aim is that the microscope development community will find it a useful tool and engage in this development to increase its general usefulness. With that aim in mind, we perform our development conversations and user support in the open as github issues and the project is an image.sc community partner. In particular, expanding the number of devices supported by Microscope would be extremely beneficial. However, adding support for a device requires physical access to the device and the current list of supported devices echoes the devices we and our collaborators have access to. This is a chicken and egg problem. Python-Microscope needs broad device support to be widely adopted by the community but it needs contributions from the community to support those devices. We believe that, Microscope currently provides enough devices and infrastructure to support adoption by more developers. There are contribution guidelines within the ``Get Involved' section of the documentation, available online at https://www.python-microscope.org/doc/get-involved.
The authors stress using their library for complex scopes but do not provide an example of complex implementation (they only provide paper references). Only a code for a simple time-series is provided. It would be very beneficial to provide the code for implementing a complex microscope and its GUI with the author's library as separate figures or in the paper's supplement. This would also support point 1 in the review.
The GUI elements provided by Python-Microscope are deliberately minimal implementations to allow basic connectivity and functionality of specific hardware to be tested. Python-Microscope is specifically designed to provide a hardware interface layer separate from the user interface. We provide a very simple examples to demonstrate how easily devices can be controlled. For more complete examples we have developed two associated packages providing GUIs, both are referenced in the text, BeamDelta is an optical alignment tool, while Microscope-Cockpit provides a full user interface to complex microscope systems. We have added a supplemental figure demonstrating the full GUI provided by Cockpit.
**Minor comments:**
It would help the paper if several phrases would be changed: Title: 'Python-Microscope: High-performance control of arbitrarily complex and scalable bespoke microscopes." To: e.g., Python-Microscope: A new open-sources Python library for the control of microscopes
Why? The authors use the word "high-performance" to address their Python library's trigger feature within the text. Unfortunately, that is not how most people would use the term for. Therefore, it should be avoided not only in the title but throughout the text. Furthermore, the word "complex" combined with microscopes should be avoided. A complex microscope is, for most microscope builders, a microscope that needs precise times and synchronization, includes several feedback active feedback loops, incorporates several devices, is very stable, etc. The context in which the term "complex microscopes" is used here is when the authors talk about the library's features to connect devices to servers either locally or remotely. I agree that the library can connect devices over arbitrary complex networks, but using the term "arbitrary complex microscopes" would be misleading considering the library's current speed limitations, the limited number of currently integrated devices, etc.
We have changed the title to:
Python-Microscope: A new open-source library for the control of microscopes
- Various section titles: "Library features" would be more suitable than "Use Cases" since the individual new features at the new library are described in this section. Also, the description of the individual features should be mentioned more accurately. The following list might be a better, more accurate fit: (1) "Device modularity" instead of "Device independence."
Also, the current title "Write once, run with any device" is inaccurate since the wrapper for multiple devices has not been implemented. (2) "Experiment- and scope-specific layout" instead of "Experiments as programs." (3) "Complex network integration" instead of "Easy implementation of complex systems and scalability" (see reasoning under point a). (4) "Hardware and software trigger integration" instead of "High performance, " (5) "Developer-friendly programming features" instead of "Simple development tool."
We have renamed the specified sections and subsections title and expanded the description in the list of use cases to be more accurate.
The authors should avoid using the term "Microscope" when talking about "Python-Microscope." It facilitates the manuscript's readability since it is occasionally not evident in the paper if they refer to the library or a microscope. We have changed “Microscope” to “Python-Microscope” in multiple places of the manuscript where it was unclear whether we were referring to the software or to a physical microscope.
The authors should avoid the phrase "pythonic software platform" in the abstract since Python-Microscope is a library / Python package and not a software platform. Furthermore, the term "pythonic" describes the desired way to write Python code. It means code that does not just get the syntax right but follows the Python community conventions and uses the language in the way it is intended to be used. Instead, it might be advisable to write, "Python-Microscope offers elegant Python-based tools to control microscopes...". We have changed the abstract as suggested.
Figure 1 should be supported by comments, e.g., #Load packages, #Parameter Initialization, #Create Devices, # Set camera parameters, etc.
Comments have been added the sample code.
The paragraph under the section "Experiments as programs" about the advantages of using Python (starting from "We have developed the software in Python, ...") should be moved into the Introduction section.
We have moved this segment to the end of the introduction.
Reviewer #2:
1)The introduction does a good job describing the current situation (using multiple software from multiple vendors simultaneously, Micro-Manager, Labview), although it could be highlighted a bit more that several groups have created custom Python code for microscope control (such as https://github.com/ZhuangLab/storm-control, https://github.com/Ulm-IQO/qudi, https://github.com/fedebarabas/tormenta, https://github.com/AndrewGYork/tools), some with at least the hope that their code will be generally usable. It also could be noted that the Micro-Manager device abstraction layer has been accessible from Python for more than a decade (currently the Python 3 interface is at https://github.com/micro-manager/pymmcore).
We have significantly expanded the references to previous Python code and made other changes to the relevant sections as detailed in the response to reviewer #1 and quoted below. We have made reference to the recently published Pycro-Manager package (the previous version referenced the arXiv preprint of this paper. It should be noted that although the Python bindings for mmcore have been available for more than a decade, they have been rarely used, the only published paper referencing them appears to be the whitepaper from a workshop on microscope control software published on arXiv in 2020 (https://arxiv.org/abs/2005.00082).
“There is currently an increasing number of software options for microscope control in Python, many of which are in the form of custom scripts specific to a microscope (Alvelid and Testa, 2019, York et al., 2013) but some provide a fully integrated microscope control environments, namely PYME https://www.python-microscopy.org/ for SMLM and ACQ4 (Campagnola et al., 2014) for electrophysiology. While this code is freely available and can be modified, their design around a specific setup, technique, or environment reduces its potential for code reuse in other projects”
2) Manuscripts describing software tools have to balance the goal to "announce" and advertise the software package with the goal to objectively explain the design principles and choices made. In my opinion, this manuscript finds a nice balance, and leaves the reader with a decent understanding of the capabilities, advantages, limitations and high level architecture of the Python-Microscope package. Possible exceptions are the use of the word "elegant" in the abstract, and extensive use of the word "bespoke" that I mainly know from real estate agent language and that likely is confusing to many readers for whom English is a second language.
We have reworded the abstract to say
“Python-Microscope offers simple to use Python-based tools to control microscopes…”
We use the term “bespoke” to refer to the construction of novel optical microscopes, as opposed to controlling existing integrated systems from commercial vendors. We have reworded paper to refer to custom built microscopes and optical systems to clarify this point.
As far as I am aware, "Microscope" is the most developed microscope abstraction layer written in pure Python. Remarkably, its design (device classes that inherit from a device-base class and have their own function calls, supplemented with "Settings" that can be declared by each device), is extremely similar to that of the Micro-Manager device abstraction layer (where "Settings" are called "Properties"), with the main difference being that one is written in Python and the other in C++ with C bindings. Writing these device classes in Python hopefully brings the advantage that more people can write them, however, the Micro-Manager C interface has the advantage that it can be used from any programming language on any platform, hence is more future proof than pure Python code. The downside of having multiple microscope device abstraction layers is that resources will be diluted and confuse partners in industry (which toolkit should they support with their limited resources?). The number of devices supported is currently much, much greater in the Micro-Manager platform than in Microscope, and a translation layer to make Micro-Manager device adapters in Microscope does not seem out of the question, and could possibly benefit many.
We are aware of the similarity between our approach and that in micromanager. There is therefore significant overlap and possible duplication of effort, however when we started this project we reviewed the Python bindings of micromanager core and felt that using this approach would add significantly, not only to our development effort, but also to end user effort as they would also have to install Micro Manager and its Python bindings. In addition, we believe that there is significant value in having a pure Python implementation. As the reviewer suggests "Python is at the moment probably the most widely used computer programming language by scientists". Having Python-Microscope in a language that the end user can code, invites them to look into the “box” and eases the process for these, possible casual, Python users to contribute with fixes and support for new devices.
Reviewer #3:
- I miss more information regarding the latency of the device-server and software triggering, how fast can it be? How much delay would you have between computers/devices? For example, could we have the devices sincronized at the microsecond range? I think this is super important so that the reader knows if it's worth using a software triggering approach with Python-Microscope or they should buy a DAQ instead. We generally expect high performance hardware to require hardware triggering, software triggers are very unlikely to be performant, or reliable enough to achieve ms, yet alone, µs timing accuracy and reproducibility. Software triggering is implemented as a basic approach to allow simple low speed hardware control, such as basic image snapping. Our systems all utilise external timing devices to provide digital triggering and, in some cases, analogue voltage control. This is becoming increasingly easy with high performance microprocessors such as the ardiuno or higher spec solutions such as National Instruments DAQ boards. We are currently investigating the recently released Raspberry Pi Pico boards, which provide very high performance digital triggering at very low cost (~£4). We are passionately promoting open source, low cost solutions, so requiring a NI DAQ board and LabView licenses goes against the spirit of this project.
1b) It's good though that they don't want to limit themselves to software triggering but also mention hardware triggering, but it's important to better explain where are the limitations.
This is a significant issue but we feel it is beyond the scope of this paper. We utilise microscope as a low level interface to hardware for our systems. The hardware control software has no internal knowledge of device connectivity eg which filter wheel might be in front of what camera, so any integrated control, such as synchronising light sources and cameras is beyond the scope of this package. We use the cockpit package as a GUI and to provide this higher level control integration. We then utilise hardware timing devices interfaced to cockpit to run experiments. We feel that this is a relatively cheap and approachable solution while allowing high performance from even complex systems.
1c) Needs info adding to the text, but in general python-microscope doesn’t concern itself with this, just allows setting of trigger types and you are then responsible for triggering.
As suggested by the reviewer, Python-Microscope does not generally concern itself with triggering. It allows setting of trigger types in a consistent manner, and on relevant devices can initiate a software trigger event. The end of the section “Fast and furious” now reads:
“The microscope interface was designed with the concept of triggers that activate the individual devices and software triggers are handled as simply another trigger type. This approach provides an interface that supports software triggers but is easily upgraded to hardware triggers. The source of such hardware triggers can be other devices --- typically a camera --- or a dedicated triggering device. The recommended procedure is to prepare an experiment template that is then loaded on a dedicated timing device which triggers all other devices, as described in Carlton 2010.
The existence of fast and cheap microprocessors and single board computers mean providing a dedicated hardware timing to sequence and synchronise a number of devices is relatively easy and extremely cost effective. We would recommend systems are designed around using an external device to provide hardware triggers to devices. This provides reliable timing and much more flexible sequencing than directly connecting outputs from one device to trigger inputs for another.”
1d) I also miss information about the triggering, do the software offer a platform that can synchronize devices, or that's more left to the developer to do? They say they can generalize to arbitrarily complex devices so therefore I think it needs to be specified how. Same with the server feature, how fast is that link?
The software triggering depends very much upon the individual devices and delays such as context switching within the OS. We offer no solution to synchronise devices. Our claim to generalise to arbitrarily complex systems is based on the fact that you can trivially run devices on different computers to allow horizontal scaling. If you wish to have 25 cameras, simply run them on different computers, then none will be speed limited by computational resources. Synchronisation can be achieved by an external hardware timing device as described above.
The server link is passed over standard ethernet, likely now 1GB/s, however data packets must be serialised before transmission and deserialised on receipt by Python, as well as standard network overhead and latency. We have only seen network limitations on image transfer from cameras to remote server computers. This has not been a significant issue as the cameras drivers typically have memory buffers, which can be enlarged to cope with backlogs, as well as the Python-Microscope image transmission processes acting on a FIFO memory queue. Possibly long experiments utilising fast, high pixel count cameras could saturate these buffers, but such a specialised application could use specialised solutions such as multi-path networking or a computer with a very large amount of RAM for temporary buffering.
2a) Some critical comments are that, first of all there are not so many drivers yet available (for example Hamamatsu camera).
The reviewer is correct, device support is critical. There are two components to this, a) the resources to implement new devices, and b) the physical hardware to enable testing and debugging of these devices. We have focused on the hardware that we own and use but hardware support is expanding. As described in our reply to reviewer #1, we hope that a community of experienced hardware and software developers will evolve and help support new devices. We have instructions on how to support new hardware devices and are happy to help interested parties. We also plan to apply for continuing funding to enable us to further develop Python-Microscope, especially to expand its range of supported hardware,
The well defined interface with the abstract base class in Python enforces what is required for a minimal implementation of a specific device type. Most devices are relatively easily supported by reference to existing devices of the same type. For instance, a stage is likely to be communicated to by serial over USB, taking simple text commands and returning easy to interpret responses. Adding a new device simply involves defining what commands to send and how to deal with the replies from the hardware. With a suitable manual this can typically be done with a few hours of programming and testing.
2b) I guess this paper is also to show proof of concept and then upon interest they will include more devices, but in that case it should be more documented how one can contribute to the project and generate new drivers. For example, if we want to try it tomorrow in our setups, and we have a specific device such as an Hamamatsu camera, What should we do? Should we contact the authors, write an issue in the github page or write the driver ourself?
We have added the following paragraph on contributing to the project at the end of discussion section of the paper:
Microscope is a free and open source project currently being used in several labs with an open development approach. Our aim is that the microscope development community will find it a useful tool and engage in this development to increase its general usefulness. With that aim in mind, we perform our development conversations and user support in the open as github issues and the project is an image.sc community partner. In particular, expanding the number of devices supported by Microscope would be extremely beneficial. However, adding support for a device requires physical access to the device and the current list of supported devices echoes the devices we and our collaborators have access to. This is a chicken and egg problem. Python-Microscope needs broad device support to be widely adopted by the community but it needs contributions from the community to support those devices. We believe that, Microscope currently provides enough devices and infrastructure to support adoption by more developers. There are contribution guidelines within the ``Get Involved' section of the documentation, available online at https://www.python-microscope.org/doc/get-involved.
- Second, the graphical interface is maybe good enough for developers and builders but in order to have a solid microscope that biologists are going to use it needs a bit more work in that direction. The GUI in microscope is extremely basic and designed for quick testing. For a microscope system aimed at biological users we would recommend using Microscope-Cockpit, our paper is now referenced and a supplemental figure shows an example of its interface, or implementing an alternative more specialised GUI. We have released Python-Microscope as a separate package to separate low level hardware control from a GUI front end, enable relatively easy automated control of microscope systems directly from Python, or allow others to create GUI base interfaces without having to deal with interfacing to specific hardware.
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Referee #3
Evidence, reproducibility and clarity
Pinto et al present a new python based software to control microscopes. Overall the work is very interesting and will help microscopists to accelerate their development by providing new tool to integrate the different hardwares.
A few aspects commented below need to be clarified to help potential future users to integrate the software for the correct microscopes/hardware.
In general the software is mostly targeted to developers that want to build microscopes, as they mention in the discussion. Some positive features are (1) the ability to have experiments as scripts, (2) the software triggering, (3) the device-server structure, and (4) the ability to have virtual devices to try out the code and the testing I see in the github page. I think it's robust especially and mostly for the device-layer of the software. It's also positive that one can install it in python and import it in your programs, so it can be incorporated into other software fairly easy.
I miss more information regarding the latency of the device-server and software triggering, how fast can it be? How much delay would you have between computers/devices? For example, could we have the devices sincronized at the microsecond range? I think this is super important so that the reader knows if it's worth using a software triggering approach with Python-Microscope or they should buy a DAQ instead. It's good though that they don't want to limit themselves to software triggering but also mention hardware triggering, but it's important to better explain where are the limitations.
I also miss information about the triggering, do the software offer a platform that can synchronize devices, or that's more left to the developer to do? They say they can generalize to arbitrarily complex devices so therefore I think it needs to be specified how. Same with the server feature, how fast is that link?
Some critical comments are that, first of all there are not so many drivers yet available (for example Hamamatsu camera). I guess this paper is also to show proof of concept and then upon interest they will include more devices, but in that case it should be more documented how one can contribute to the project and generate new drivers. For example, if we want to try it tomorrow in our setups, and we have a specific device such as an Hamamatsu camera, What should we do? Should we contact the authors, write an issue in the github page or write the driver ourself?
Second, the graphical interface is maybe good enough for developers and builders but in order to have a solid microscope that biologists are going to use it needs a bit more work in that direction.
Significance
Microscope control software, especially is open source, can help the rapid integration of new hardware and accelerate overall microscopy development.
I see this paper as an important starting point platform for future more user friendly Python-microscope controlling software.
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Referee #2
Evidence, reproducibility and clarity
This manuscript describes Python-Microscope, a library/framework written in Python to control custom-built microscopes. Modern light microscopes consist of many computer controllable components and data sensors, and software has become an integral component of such systems. Microscopy is such a fast moving and diverse technology that a significant (>25%?) fraction of microscope systems can not be cookie-cutter, standardized systems, but are custom-built, assembled using commercial microscope stands and/or hardware from vendors such as Thorlabs. For many, creating the software to control such custom-built systems is more laborious and difficult than building the actual optical setup, and software toolkits to make this easier (such as the one presented in this manuscript) are of great interest to everyone working in this area. Python is at the moment probably the most widely used computer programming language by scientists, and a well-thought-out environment for microscope control from the Python language is a welcome addition.
The introduction does a good job describing the current situation (using multiple software from multiple vendors simultaneously, Micro-Manager, Labview), although it could be highlighted a bit more that several groups have created custom Python code for microscope control (such as https://github.com/ZhuangLab/storm-control, https://github.com/Ulm-IQO/qudi, https://github.com/fedebarabas/tormenta, https://github.com/AndrewGYork/tools), some with at least the hope that their code will be generally usable. It also could be noted that the Micro-Manager device abstraction layer has been accessible from Python for more than a decade (currently the Python 3 interface is at https://github.com/micro-manager/pymmcore).
Manuscripts describing software tools have to balance the goal to "announce" and advertise the software package with the goal to objectively explain the design principles and choices made. In my opinion, this manuscript finds a nice balance, and leaves the reader with a decent understanding of the capabilities, advantages, limitations and high level architecture of the Python-Microscope package. Possible exceptions are the use of the word "elegant" in the abstract, and extensive use of the word "bespoke" that I mainly know from real estate agent language and that likely is confusing to many readers for whom English is a second language.
As far as I am aware, "Microscope" is the most developed microscope abstraction layer written in pure Python. Remarkably, its design (device classes that inherit from a device-base class and have their own function calls, supplemented with "Settings" that can be declared by each device), is extremely similar to that of the Micro-Manager device abstraction layer (where "Settings" are called "Properties"), with the main difference being that one is written in Python and the other in C++ with C bindings. Writing these device classes in Python hopefully brings the advantage that more people can write them, however, the Micro-Manager C interface has the advantage that it can be used from any programming language on any platform, hence is more future proof than pure Python code. The downside of having multiple microscope device abstraction layers is that resources will be diluted and confuse partners in industry (which toolkit should they support with their limited resources?). The number of devices supported is currently much, much greater in the Micro-Manager platform than in Microscope, and a translation layer to make Micro-Manager device adapters in Microscope does not seem out of the question, and could possibly benefit many.
Expected audience:
This manuscript will be of interest to those scientists who build/assemble their own microscope systems and write software code to control their operation.
Field of expertise:
I think a lot about microscope control software and how it can help scientists do their experiments.
Significance
see above.
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Referee #1
Evidence, reproducibility and clarity
Summary:
In this manuscript, Pinto et al. report Python-Microscope, a new open-source Python library for microscopy control. The new library lets microscope builders implement individual microscope devices as Python Classes with devices specific parameters and methods. Furthermore, the new Python library supports remote procedural calls and turns individual devices into a resource accessible over a network. Moreover, it has been designed to support hardware as well as software triggers. Finally, it provides several developer-friendly features; it is equipped with simple GUI programs for different device types, and it can simulate devices without the need for physical access to the hardware.
Major comments:
- The authors highlight in their conclusion that the new Python library has the potential to accelerate and expand microscopy development. I agree with this statement since classes and methods do not need to be written in Python from scratch anymore. However, I would recommend that the authors include in their conclusion the value of the library for reproducibility if the final python acquisition code is shared along with publications. Nowadays, scientists frequently write in their publications that LabView or a specific commercial scope's acquisition software was used without any acquisition code. Python-Microscope would have the potential to change this trend, and the authors need to stress this aspect and its value for reproducibility in science accordingly.
- The authors need to provide a more comprehensive overview of the currently used data acquisition strategies in their introduction. Currently, they highlight the acquisition software provided by vendors for data acquisition (mainly used by life scientists and not necessary scope builders/developers), Micro-Manager (mainly used by life scientists; currently also restricted to wide-field systems), and LabView (for advanced microscope systems; used by advanced developers). However, most advanced microscope builders use MatLab (Chmyrov et al. Nature Methods (2013) - https://doi.org/10.1038/nmeth.2556, Ta et al. Nature Communications (2015) - https://doi.org/10.1038/ncomms8977 , etc.), Python (York et al. Nature Methods (2013) - https://doi.org/10.1038/nmeth.2687, etc.), and LabView to write their acquisition software. Since the manuscript focused on advanced microscopes, the authors need to position their library with respect to Matlab and Python's current use as well.
- The authors need to give (1) software provided by vendors, (2) LabView, and (2) Micro-Manager, more credit. (1) Several microscope vendors (e.g., Abberior Instruments - https://imspectordocs.readthedocs.io/en/latest/specpy.html ) allow their scopes can be externally controlled to enable the execution of customer-driven acquisition strategies which the vendor's acquisition software itself might not have implemented with. The authors might want to include that scope vendors aim for more customer modifiable acquisition software. (2) The authors criticize that LabView code can be hard to understand, reproduce and maintain. However, similar to writing good code in general, there are best practice strategies for writing good LabView code to ensure scalability, readability, and maintainability available as well (https://learn.ni.com/learning-paths/labview-core-3-2016-english ). The primary problem might lie more on the side of lousy coding practice than on LabView's side to perform appropriately. (3) The authors should include the current effort by Pinkard et al. (Pinkard et al. Nature Methods (2021) - https://doi.org/10.1038/s41592-021-01087-6 ) in their discussion.
- The authors might want to explain how they plan to facilitate the library's adoption and the long-term maintenance within the microscopy community. Do they plan to create a new category on Image.sc, which would allow the community to interact with the developers? etc. Furthermore, who will keep writing wrappers to the libraries provided by the vendors? etc Several useful software packages have been written in the past, but their existence was often not for long (after 2-3 years, most packages simply can not be used anymore). The concept of software maintenance is frequently not addressed/considered. Therefore, could the authors expand this aspect in an additional section of their paper?
- The authors stress using their library for complex scopes but do not provide an example of complex implementation (they only provide paper references). Only a code for a simple time-series is provided. It would be very beneficial to provide the code for implementing a complex microscope and its GUI with the author's library as separate figures or in the paper's supplement. This would also support point 1 in the review.
Minor comments:
- It would help the paper if several phrases would be changed: a. Title: 'Python-Microscope: High-performance control of arbitrarily complex and scalable bespoke microscopes." To: e.g., Python-Microscope: A new open-sources Python library for the control of microscopes Why? The authors use the word "high-performance" to address their Python library's trigger feature within the text. Unfortunately, that is not how most people would use the term for. Therefore, it should be avoided not only in the title but throughout the text. Furthermore, the word "complex" combined with microscopes should be avoided. A complex microscope is, for most microscope builders, a microscope that needs precise times and synchronization, includes several feedback active feedback loops, incorporates several devices, is very stable, etc. The context in which the term "complex microscopes" is used here is when the authors talk about the library's features to connect devices to servers either locally or remotely. I agree that the library can connect devices over arbitrary complex networks, but using the term "arbitrary complex microscopes" would be misleading considering the library's current speed limitations, the limited number of currently integrated devices, etc. b. Various section titles: "Libraray features" would be more suitable than "Use Cases" since the individual new features at the new library are described in this section. Also, the description of the individual features should be mentioned more accurately. The following list might be a better, more accurate fit: (1) "Device modularity" instead of "Device independence." Also, the current title "Write once, run with any device" is inaccurate since the wrapper for multiple devices has not been implemented. (2) "Experiment- and scope-specific layout" instead of "Experiments as programs." (3) "Complex network integration" instead of "Easy implementation of complex systems and scalability" (see reasoning under point a.) (4) "Hardware and software trigger integration" instead of "High performance, " (5) "Developer-friendly programming features" instead of "Simple development tool." c. The authors should avoid using the term "Microscope" when talking about "Python-Microscope." It facilitates the manuscript's readability since it is occasionally not evident in the paper if they refer to the library or a microscope. d. The authors should avoid the phrase "pythonic software platform" in the abstract since Python-Microscope is a library / Python package and not a software platform. Furthermore, the term "pythonic" describes the desired way to write Python code. It means code that does not just get the syntax right but follows the Python community conventions and uses the language in the way it is intended to be used. Instead, it might be advisable to write, "Python-Microscope offers elegant Python-based tools to control microscopes...".
- Figure 1 should be supported by comments, e.g., #Load packages, #Parameter Initialization, #Create Devices, # Set camera parameters, etc.
- The paragraph under the section "Experiments as programs" about the advantages of using Python (starting from "We have developed the software in Python, ...") should be moved into the Introduction section.
Significance
The field of microscopy emphasizes more and more openness and transparency of methods and tools being used to accelerate science, but also to guarantee reproducibility.
The authors' library is another step in the right direction. It is open, transparent, tries to satisfy multiple tool developers' needs to make the development of microscopes faster, easier, and more approachable/user-friendly. Although it can not yet be used for arbitrarily complex microscopes, it has the potential to do so in the future. For now, the authors need to manage to incorporate and involve microscopy developers' needs and requirements in the best possible way to be able to design the library as holistic as possible.
I am a physicist and microscope builder and have so far used MatLab, LabView, and Imspector as well as Python scripts to control microscopes, and I will definitely test the authors' library on my own.
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www.biorxiv.org www.biorxiv.org
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Reply to the reviewers
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We thank the reviewers for their constructive and critical feedback on our original manuscript.
Reviewer #1 (Evidence, reproducibility and clarity (Required)): In this study, the authors explored the tissue-specific regulation of DT size using both global and targeted deletion of Fgf9. They found cell hypertrophy and mineralization dynamics of the DT, as well as transcriptional signatures from skeletal muscle but not bone, were influenced by the global loss of Fgf9. Deletion of Fgf9 in skeletal muscle leads to postnatal enlargement of the DT. However, the innovation of this paper is not enough, the phenotypes of global deletion of Fgf9 were previously reported, most of the data in this paper are mainly descriptive analysis of the phenotypes, and internal cellular and molecular mechanisms were not well investigated.
Here are the major issues:
1.The data showed that fewer osteoclasts were present at both E16.5 and P0 in Figure 2R, V. Whether FGF9 affects both osteogenesis and osteoclast formation?
- Authors’ response to Reviewer: Thank you for your feedback. We revised this manuscript to reflect the concerns of Reviewer 1 related to the lack of cellular and molecular mechanisms as described below. **Based on this question from the Reviewer, we have revised our discussion to clarify our findings as follows: “From our EdU proliferation assays, we observed a decline in cell proliferation in Fgf9null attachments, suggesting an accelerated chondrocyte maturation. Though we saw similar levels of Pthlh expression (a chondrocyte hypertrophy suppressor) in both WT and Fgf9null attachments, we also saw increased expression of Gli1 (a marker of chondrocyte hypertrophy) localized to the attachment in Fgf9null embryos compared to WT embryos. This decrease in proliferation was in parallel with increased hypertrophy of chondrocytes adjacent to the attachment cells within the Fgf9null DT, which may have led to a rapid expansion of matrix in the DT. Even though the DT was enlarged in Fgf9null mutants, we found fewer Sost+ cell clusters in their DTs compared to WT mice. Mature osteocytes express Sost (Winkler et al., 2003), and fewer Sost+ cells may indicate an impaired ability of Fgf9null osteoblasts to embed and mature into osteocytes. Overexpression of FGF9 in the perichondrium has been previously shown to suppress chondrocyte proliferation and limit bone growth in the limb (Karuppaiah et al., 2016); in our study, we found that loss of Fgf9 globally leads to an accelerated enlargement of chondrocytes in the tuberosity. This accelerated enlargement may limit the ability of these cells to deposit matrix and mineral and therefore limit osteocyte differentiation. We also found fewer osteoclasts in the Fgf9null DT which mirrors previous reports using the same mutation to study the length and vascularity of developing limb (Hung et al., 2007). Because the DT is enlarged and resides on the surface of a shortened bone, this phenotype may elucidate a divergent role of FGF9 in patterning of an arrested (e.g., attachment) growth plate compared to a regular (e.g., long bone) growth plate. This includes unexplored roles of FGF9 in vascularity of the tendon attachment and formation of bone ridges that overlap with or deviate from its role in growth plate development that are beyond the scope of the current study.”
- RNA-sequencing analysis showed the decreased expression of mitochondria/ energy and lipid associated genes in Fgf9 null muscle compared to WT muscle, how does this relate to the enlargement of the DT? What are the detailed molecular mechanisms?
- Authors’ response to Reviewer:
- Based on this question from the Reviewer, we have revised our discussion to reflect the potential molecular mechanisms related to muscle mitochondria, fiber type, and metabolism as follows:
“Fgf9 is expressed in muscle during embryonic stages, which we and others have observed using ISH (Colvin et al., 1999; Garofalo et al., 1999; Hung et al., 2007; Yang and Kozin, 2009). Previous work has established a connection between Fgf9 and muscle, as treatment of muscle and muscle progenitor cells with FGF9 slows maturation, enhances proliferation, and decreases expression of various myogenic genes (Huang et al., 2019). This study found supporting evidence that Fgf9 expression in muscle may be a limiting factor in tuberosity growth. However, it remains unknown how other FGFs and their receptors, FGFRs, regulate superstructure and attachment formation. In this study, we identified potential mediators of skeletal muscle metabolism in Fgf9null muscle, including downregulated mitochondrial-related genes associated with oxidative respiration and proton transport (i.e., Slc36a2 and Ucp1, amongst others). In cultured myoblasts, FGF9 can inhibit myogenic differentiation potentially via increased production of Myostatin (Huang et al., 2019), a well-established mediator of fast glycolytic muscle fibers (Girgenrath et al., 2005; Hennebry et al., 2009). While the role of FGF9 in myoblast fusion has been investigated in vitro, its effect on muscle fiber type and fiber metabolism (i.e., oxidative vs. glycolytic) has not yet been explored. Our findings from bulk RNA-seq of Fgf9null muscle point to potential mechanisms in muscle metabolism that may contribute to the enlarged phenotype that is mimetic of that found in Myostatin deficient mice and other animals (Elkasrawy and Hamrick, 2010; Hamrick et al., 2002). Additionally, further investigations are needed to investigate the potential role of Fgf9 in mitochondrial function and lipid metabolism. Recent work by Huang et al. also identified FGF9 as a potent regulator of calcium signaling and homeostasis in myoblast culture in vitro, and calcium release from the sarcoplasmic reticulum in muscle plays a critical role during embryonic skeletal myogenesis via ryanodine receptor 1 (RYR1). Although Ryr1 was not significantly different in between Fgf9null and WT muscle in the present study, we did find that calmodulin-associated genes (e.g., Calm4, Calml3, Camsap3, Calm5) were all significantly upregulated in Fgf9null muscle compared to WT muscle. Calmodulin interacts with RYR1 and its activation is required for intracellular binding of calcium (Newman et al., 2014, 1). Calmodulin is a crucial component of the calcium signal transduction pathway and also plays an important role in lipid and glucose metabolism (Nishizawa et al., 1988). Taken together, our findings along with recent work by Huang et al. support more mechanistic studies to investigate the metabolic effects of loss and gain of function of Fgf9 on skeletal muscle as well as the muscle secretome.”
Reviewer #1 (Significance (Required)):
R1 The authors compared the phenotypes between globally and muscle-specifically deletion of Fgf9 in mice, and found that Fgf9 secreted by muscle may induced the enlargement of the DT. However, the detailed molecular mechanisms were not well investigated.
**Referees cross-commenting**
R2 I do not disagree with Rev 1, but I do not think such a task is so trial reason why I don't suggest; it could take years to determine molecular mechanisms of anything. The authors could expand the discussion, offer some possibilities. If they had some RNAseq data they maybe could suggest some of the key signaling pathways involved.
**Referees cross-commenting**
R1 We still suggested that the internal cellular and molecular mechanisms should be well investigated in this papaer.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
- This paper deals with an important topic which is exact molecular mechanisms regulating the growth of bony tuberosities; because this region is essential for force transmission and movement.
- Based on the previous information they had that in the global KO of the gene FGF9 the deltoid muscle is enlarged; and this muscle is in a very important tuberosity; they decided to look at FGF9 as a potential genetic regulator.
The manuscript is clear, objective, concise. Very clear. Authors used both the global and targeted deletions, very high reproducibility. Reviewer #2 (Significance (Required)):
This manuscript advances several areas since we know little about the mechanisms controlling local mechanisms of tuberosities. It also advances our knowledge of FGF9. There were several studies before mostly in vitro showing that FGF9 when added to muscle cells could arrest myogenesis, but the types of experiments in vivo had not been performed yet. The authors used an array of methods; the studies are unbiased and very rigorous and also they always show all experimental points, which is excellent. The conclusions are supported by the data.
- The main suggestion for authors: They essentially do not discuss the nature of the potential muscle to bone signaling occurring when they target the deletion of FGF9 in skeletal muscles and muscles enlarge and there is a series of adaptions in the tuberosity. Do the authors believe this to be all the genetic changes or potentially through secreted myokines? In the paper of Huang et al, 2019 the authors document an effect of FGF9 in intracellular calcium homeostasis/signaling; could this be part of the mechanism? Perhaps the authors could propose a model?
Authors’ response to Reviewer:
- Future studies could investigate the secretome of muscle in Fgf9null or muscle-specific knockouts, as well as assess calcium signaling homeostasis in Fgf9 mutant muscles. We did find calcium- and ion-associated genes in the RNAseq and revised the discussion to include this information.
- Based on this question from the Reviewer, we have revised our discussion to reflect the potential molecular mechanisms related to muscle mitochondria, fiber type, and metabolism as follows: “Fgf9 is expressed in muscle during embryonic stages, which we and others have observed using ISH (Colvin et al., 1999; Garofalo et al., 1999; Hung et al., 2007; Yang and Kozin, 2009). Previous work has established a connection between Fgf9 and muscle, as treatment of muscle and muscle progenitor cells with FGF9 slows maturation, enhances proliferation, and decreases expression of various myogenic genes (Huang et al., 2019). This study found supporting evidence that Fgf9 expression in muscle may be a limiting factor in tuberosity growth. However, it remains unknown how other FGFs and their receptors, FGFRs, regulate superstructure and attachment formation. In this study, we identified potential mediators of skeletal muscle metabolism in Fgf9null muscle, including downregulated mitochondrial-related genes associated with oxidative respiration and proton transport (i.e., Slc36a2 and Ucp1, amongst others). In cultured myoblasts, FGF9 can inhibit myogenic differentiation potentially via increased production of Myostatin (Huang et al., 2019), a well-established mediator of fast glycolytic muscle fibers (Girgenrath et al., 2005; Hennebry et al., 2009). While the role of FGF9 in myoblast fusion has been investigated in vitro, its effect on muscle fiber type and fiber metabolism (i.e., oxidative vs. glycolytic) has not yet been explored. Our findings from bulk RNA-seq of Fgf9null muscle point to potential mechanisms in muscle metabolism that may contribute to the enlarged phenotype that is mimetic of that found in Myostatin deficient mice and other animals (Elkasrawy and Hamrick, 2010; Hamrick et al., 2002). Additionally, further investigations are needed to investigate the potential role of Fgf9 in mitochondrial function and lipid metabolism. Recent work by Huang et al. also identified FGF9 as a potent regulator of calcium signaling and homeostasis in myoblast culture in vitro, and calcium release from the sarcoplasmic reticulum in muscle plays a critical role during embryonic skeletal myogenesis via ryanodine receptor 1 (RYR1). Although Ryr1 was not significantly different in between Fgf9null and WT muscle in the present study, we did find that calmodulin-associated genes (e.g., Calm4, Calml3, Camsap3, Calm5) were all significantly upregulated in Fgf9null muscle compared to WT muscle. Calmodulin interacts with RYR1 and its activation is required for intracellular binding of calcium (Newman et al., 2014, 1). Calmodulin is a crucial component of the calcium signal transduction pathway and also plays an important role in lipid and glucose metabolism (Nishizawa et al., 1988). Taken together, our findings along with recent work by Huang et al. support more mechanistic studies to investigate the metabolic effects of loss and gain of function of Fgf9 on skeletal muscle as well as the muscle secretome.
In conclusion, this work established a new role of skeletal muscle derived Fgf9 during skeletal development and tuberosity growth. Additionally, our unbiased transcriptomic approaches and rigorous analyses identified new potential mechanisms associated with muscle development, mitochondrial bioenergetics, and muscle metabolism that warrant further investigation into the role of FGF9 in muscle-bone crosstalk.”
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Referee #2
Evidence, reproducibility and clarity
This paper deals with an important topic which is exact molecular mechanisms regulating the growth of bony tuberosities; because this region is essential for force transmission and movement. Based on the previous information they had that in the global KO of the gene FGF9 the deltoid muscle is enlarged; and this muscle is in a very important tuberosity; they decided to look at FGF9 as a potential genetic regulator.
The manuscript is clear, objective, concise. Very clear. Authors used both the global and targeted deletions, very high reproducibility.
Significance
This manuscript advances several areas since we know little about the mechanisms controlling local mechanisms of tuberosities. It also advances our knowledge of FGF9. There were several studies before mostly in vitro showing that FGF9 when added to muscle cells could arrest myogenesis, but the types of experiments in vivo had not been performed yet. The authors used an array of methods; the studies are unbiased and very rigorous and also they always show all experimental points, which is excellent. The conclusions are supported by the data.
The main suggestion for authors: They essentially do not discuss the nature of the potential muscle to bone signaling occurring when they target the deletion of FGF9 in skeletal muscles and muscles enlarge and there is a series of adaptions in the tuberosity. Do the authors believe this to be all the genetic changes or potentially through secreted myokines? In the paper of Huang et al, 2019 the authors document an effect of FGF9 in intracellular calcium homeostasis/signaling; could this be part of the mechanism? Perhaps the authors could propose a model?
Referees cross-commenting
I do not disagree with Rev 1, but I do not think such a task is so trial reason why I don't suggest; it could take years to determine molecular mechanisms of anything. The authors could expand the discussion, offer some possibilities. If they had some RNAseq data they maybe could suggest some of the key signaling pathways involved.
-
Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.
Learn more at Review Commons
Referee #1
Evidence, reproducibility and clarity
In this study, the authors explored the tissue-specific regulation of DT size using both global and targeted deletion of Fgf9. They found cell hypertrophy and mineralization dynamics of the DT, as well as transcriptional signatures from skeletal muscle but not bone, were influenced by the global loss of Fgf9. Deletion of Fgf9 in skeletal muscle leads to postnatal enlargement of the DT. However, the innovation of this paper is not enough, the phenotypes of global deletion of Fgf9 were previously reported, most of the data in this paper are mainly descriptive analysis of the phenotypes, and internal cellular and molecular mechanisms were not well investigated.
Here are the major issues:
1.The data showed that fewer osteoclasts were present at both E16.5 and P0 in Figure 2R, V. Whether FGF9 affects both osteogenesis and osteoclast formation?
2.RNA-sequencing analysis showed the decreased expression of mitochondria/ energy and lipid associated genes in Fgf9 null muscle compared to WT muscle, how does this relate to the enlargement of the DT? What are the detailed molecular mechanisms?
Significance
The authors compared the phenotypes between globally and muscle-specifically deletion of Fgf9 in mice, and found that Fgf9 secreted by muscle may induced the enlargement of the DT. However, the detailed molecular mechanisms were not well investigated.
Referees cross-commenting
We still suggested that the internal cellular and molecular mechanisms should be well investigated in this papaer.
-
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Reply to the reviewers
Dear Dr. Monaco,
Thank you for reviewing our manuscript entitled ‘Discovery of re-purposed drugs that slow SARS-CoV-2 replication in human cells’. We are pleased to see that the reviewers make suggestions that will strengthen the paper. With cases of COVID-19 rising at dramatic levels in some parts of the world, we are anxious to see our results published in a peer-review journal.
Please find below a detailed response to the comments is shown in bold. We can perform the additional experiments and make changes to the manuscript within 3 weeks of a journal agreeing to consider our paper.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
**Summary:**
Pickard et al. present in the manuscript entitled "Discovery of re-purposed drugs that slow SARS-CoV-2 replication in human cells" a new screen of FDA approved drugs against SARS-CoV-2. The authors based their screen on Vero and HUH7 cell lines. The methods applied for screening including the SARS-Cov-2-ΔOrf7a-NLuc modified virus are properly designed and preformed. This is an interesting study that finds several potential drugs that might be effective as anti SARS-CoV-2 therapies. However, such experiments have been done throughout the last year and the novelty and importance of these findings are questionable.
Regarding this point, there are several studies that have attempted to identify compounds that impact on SARS-Cov2 infection; however, these do not specifically focus on the replication of the virus (studies have used viability markers and staining of viral proteins but many of the compounds identified exert their effects on the virus uptake). Whilst SARS-CoV2-Nluc viruses have been developed these have been used for infection studies to measure the amount of virus taken up by cells and have not further explored how they impact on virus replication. Therefore, we feel that our study shows that a reporter virus can be used to reflect virus replication.
**Major comments:**
- Most the experiments presented are only done twice, while in the screen itself it should not be a problem, for verifying the drugs identified at least three experiments are suggested (Figure 5 and Supplemental Figure 6) At the time of submission there was an urgent need to make our data accessible to the scientific community. Therefore, we performed some experiments with n=2. We used n=2 to validate the screen and each time we got the same experimental outcome. We would perform further repeats for the figures mentioned for publication.
To strengthen the results of the screen, the wild type virus should also be tested for plaque reduction assay with these nine drugs.
We will perform these experiments and present these data in the manuscript. We have already performed immunostaining of WT-virus infected cells and could include this as an alternative.
Identification of antivirals is important for SARS-CoV-2 and other coronaviruses, regardless of the presence or effectiveness of vaccines. I think the abstract and introduction should be written to emphasize this point (instead of trying to underestimate the vaccine effectiveness). Similarly, the authors ignore the relative failures of known antivirals (known to inhibit SARS-CoV-2 replication in vitro like Remdesavir) in clinical trials and suggest starting clinical trials with their screen results. I think that this suggestion is premature and require several more studies (including animals studies) before initiating clinical trials.
We will re-write this section of the manuscript. We have identified all compounds that have been evaluated in the AGILE clinical trial, and these compounds failed to show a patient benefit and also failed to impact on virus replication in human cells.
**Minor comments.**
- The errors bars are not defined throughout all the figures. I am not sure that error bars are even meaningful if experiments only done twice, I recommend showing the two results for each point. We will add additional repeats or as the reviewer suggests we could add the two points.
Figure 1E and the tables especially supp tables 3 and 4? don't have legends.
Apologies, this will be amended.
Most graphs will benefit from presenting the results in logarithmic scale (all Luc counts/ qPCRs).
This can be changed if editors agree.
P6 in the Generation of functional SARS-CoV-2 virus section - a reference is missing "It has been reported that this aids the recovery of replicative virus (Insert ref 3)"
Apologies, this will be amended.
Reviewer #1 (Significance (Required)):
This is a well performed drug screen on two cell lines that identified new potential FDA approved drugs as anti-SARS-CoV-2 inhibitors. There are several studies that already been published or distributed as preprints that have done similar experiments in other cells lines including more relevant lung epithelial cells (for example PMC743673). This study does not verify the screen results by additional methods. However, in the current pandemic situation this study could be important and interesting to follow up.
I am a virologist; my expertise is in viral host interactions within infected cell.
We were unable to identify the paper which is referred to in the reviewer’s comments. We would aim to highlight further in the text that using the reporter virus, we are able to screen and identify compounds that impact on virus replication unlike many of the other studies.
**Referee Cross-commenting**
No problem with the other comments
Reviewer #2 (Evidence, reproducibility and clarity (Required)): **Summary:**
In this manuscript, the authors report on the creation of a luciferase-encoding SARS-CoV-2 (deleted for orf7a) and the use of this virus to test infectability of multiple cell lines as well as perform a drug repurposing screen in two cell lines (Vero E6 and Huh7). Of the 35 drugs that blocked the virus replication they further identify 9 drugs that have a (mild) effect on replication when administered 24 hours post infection.
An important note here is that many studies which have identified potential therapeutics for SARS-Cov2 have performed experiments whereby cells are pre-treated with compounds prior to infection. We have been able to performed the same experiments and many of the drugs were unable to prevent replication after infection. The 9 compounds we have identified retain the ability to inhibit replication when applied post-infection. This sets our study apart from other screens that have been conducted for SARS-Cov2.
**Major comments:**
- Figure 2: What's the difference between "Luminescence counts above noise" in Fig 2B and "Luminescence counts per second" in Figure 2C,D ? It seems like there is no difference in luminescence between 1 PFU and 100 PFU (and if anything, the bassline for 1PFU is higher, >1.5M, compared to 100 PFU where is below 1M). One would expect more luminescence in the 100 PFU experiment, as seen in Fig 2B. Also in Fig 2B it does not mention how many replicates, or what does the **** stands for. Thank you for the comment. The difference in “luminescence counts above noise” and “luminescence counts per second” is set out in Figure 2A. When adding more virus the baseline level should increase, as also demonstrated in Supplemental Figure 3. However, the degree of background luminescence varies between virus batches, presumably due to the degree of cell lysis in each sample. You will note in the Supplemental figure that the baseline levels for our P4 viral stock is lower than P1. We performed the experiments in Figure 2C using virus P1 virus stocks and for Figure 2D we used P4 virus. For clarity this information will be included in the figure legend and the data presented at luminescence over background.
The authors do not explain why deleting orf7a was needed to generate the NLuc virus. Was there a rational for this?
Orf7a has been successfully removed from SARS-CoV and SARS-CoV2 in order to incorporate traceable proteins such as fluorescent or bioluminescent proteins. We describe this at the start of the results section. “Orf7a has previously been removed in SARS-CoV and SARS-CoV-2 and yielded infectious and replicative virus particles (Thi Nhu Thao et al, 2020; Xie et al, 2020a; Xie et al, 2020b)”.
Figure 5C - IC50 should be properly determined from compounds where the lowest concentration tested was still inhibitory (such as LY2835219 and panobinostat).
These experiments can be conducted, within 2 weeks. However we do not feel that this would provide additional information to the reader. The aim of these figures is to demonstrate that there are dose dependent effects of these compounds on the replication of SARS-CoV2.
Supplementary tables must be provided in an excel or similar file format. The PDF version is both unreadable and does not allow other researchers to probe the dataset for their own interests.
This would be amended during revision of our submission.
**Minor comments:**
- Intro: "SARS-CoV-2 infection in patients with COVID-19 can result in pulmonary distress, inflammation, and broad tissue tropism". Broad tissue tropism is not a result of infection, please rephrase. Patients with COVID-19 are reported to have liver and kidney damage. This could be a direct result of SARS-CoV2 infection or indirectly via the cytokine storm. Our data shows that kidney and liver cells are highly susceptible to SARS-CoV2 infection and support replication, in culture. We thank the reviewer for their comment and we will rephrase this statement and cite relevant literature.
Fig S1D - why are the MOI different for WT (moi 0.1) and NLuc mutant (moi 1) ?
This was used to demonstrate the lack of replication of the WT virus in lung epithelial cells, the same MOI used in Vero cells demonstrates that the levels of the nucleocapsid protein increases when compared to other cell types. We have also used an MOI of 10 for the NLuc virus to be able to detect the NLuc protein. This information would be added to the figure legend.
Fig S3 - using volume of virus in ul is problematic, as it doesn't allow for proper comparison between the passages. The author would express the virus amount in PFU or MOI.
This will be amended
Fig S5 - in panel A - what do the colors represent? What is 0-1?. The number of repetitions for each panel should be indicated.
Apologies, relative expression should have been added alongside the scale. N=3 for this experiments this will be added to the figure legend.
The "NLuc activity as a marker of virus replication" and "SARS-CoV-2 replication screen validation" are largely overlapping and should be edited.
We would combine these sections.
Methods: "Generation of functional SARS-CoV-2 virus" - the author confuse "virus" with "plasmid". They should also include the reference marked "(Insert ref 3)"
Apologies, this will be amended
Reviewer #2 (Significance (Required)):
- My main concern is that a very similar, if not identical, NLuc encoding virus has been reported in October 2020 (https://www.nature.com/articles/s41467-020-19055-7#Sec9). While the authors cite this paper, they only do so to say that "Orf7a has previously been removed in SARS-CoV and SARS-CoV-2 and yielded infectious and replicative virus particles", without mentioning this was done to generate the same NLuc carrying virus reported in their work. Thus the generation of this virus is not a "new tool" as the authors would seem to suggest. Whilst this is not the first use of a NLuc SARS-CoV2 virus, this is the first time that the virus has been utilised to screen for compounds that effect replication. The study mentioned does not screen nor monitor the replication of the virus, the authors do monitor the capability of the virus to infect cells only during the first 24 hours.
While drug repurposing screens have been performed, the addition validation in Vero E6 and Huh7 cells is of some interest to those working on anti-viral therapies, given that the authors change their supplementary tables to a format that can be accessible by other researchers.
This will be amended for the submission.
My expertise: I study virus-host interactions (not coronaviruse). In the last year I have been involved in several drug repurposing efforts against SARS-CoV-2.
**Referee Cross-commenting**
No problem with the other comments.
-
Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.
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Referee #2
Evidence, reproducibility and clarity
Summary:
In this manuscript, the authors report on the creation of a luciferase-encoding SARS-CoV-2 (deleted for orf7a) and the use of this virus to test infectability of multiple cell lines as well as perform a drug repurposing screen in two cell lines (Vero E6 and Huh7). Of the 35 drugs that blocked the virus replication they further identify 9 drugs that have a (mild) effect on replication when administered 24 hours post infection.
Major comments:
- Figure 2: What's the difference between "Luminescence counts above noise" in Fig 2B and "Luminescence counts per second" in Figure 2C,D ? It seems like there is no difference in luminescence between 1 PFU and 100 PFU (and if anything, the bassline for 1PFU is higher, >1.5M, compared to 100 PFU where is below 1M). One would expect more luminescence in the 100 PFU experiment, as seen in Fig 2B. Also in Fig 2B it does not mention how many replicates, or what does the ** stands for.
- The authors do not explain why deleting orf7a was needed to generate the NLuc virus. Was there a rational for this?
- Figure 5C - IC50 should be properly determined from compounds where the lowest concentration tested was still inhibitory (such as LY2835219 and panobinostat).
- Supplementary tables must be provided in an excel or similar file format. The PDF version is both unreadable and does not allow other researchers to probe the dataset for their own interests.
Minor comments:
- Intro: "SARS-CoV-2 infection in patients with COVID-19 can result in pulmonary distress, inflammation, and broad tissue tropism". Broad tissue tropism is not a result of infection, please rephrase.
- Fig S1D - why are the MOI different for WT (moi 0.1) and NLuc mutant (moi 1) ?
- Fig S3 - using volume of virus in ul is problematic, as it doesn't allow for proper comparison between the passages. The author would express the virus amount in PFU or MOI.
- Fig S5 - in panel A - what do the colors represent? What is 0-1?. The number of repetitions for each panel should be indicated.
- The "NLuc activity as a marker of virus replication" and "SARS-CoV-2 replication screen validation" are largely overlapping and should be edited.
- Methods: "Generation of functional SARS-CoV-2 virus" - the author confuse "virus" with "plasmid". They should also include the reference marked "(Insert ref 3)"
Significance
- My main concern is that a very similar, if not identical, NLuc encoding virus has been reported in October 2020 (https://www.nature.com/articles/s41467-020-19055-7#Sec9). While the authors cite this paper, they only do so to say that "Orf7a has previously been removed in SARS-CoV and SARS-CoV-2 and yielded infectious and replicative virus particles", without mentioning this was done to generate the same NLuc carrying virus reported in their work. Thus the generation of this virus is not a "new tool" as the authors would seem to suggest.
- While drug repurposing screens have been performed, the addition validation in Vero E6 and Huh7 cells is of some interest to those working on anti-viral therapies, given that the authors change their supplementary tables to a format that can be accessible by other researchers.
My expertise: I study virus-host interactions (not coronaviruse). In the last year I have been involved in several drug repurposing efforts against SARS-CoV-2.
Referee Cross-commenting
No problem with the other comments.
-