Reviewer #2 (Public Review):

Summary:

In this work, the authors attempt to noninvasively image metabolic aspects of the tumor microenvironment in vivo, in 2 mouse models of glioblastoma. The tumor lesion and its surrounding appearance are extensively characterized using histology to validate/support any observations made with the metabolic imaging approach. The metabolic imaging method builds on a previously used approach by the authors and others to measure the kinetics of deuterated glucose metabolism using dynamic 2H magnetic resonance spectroscopic imaging (MRSI), supported by de-noising methods.

Strengths:

Extensive histological evaluation and characterization.

Measurement of the time course of isotope labeling to estimate absolute flux rates of glucose metabolism.

Weaknesses:

The de-noising method appears essential to achieve the high spatial resolution of the in vivo imaging to be compatible with the dimensions of the tumor microenvironment, here defined as the immediately adjacent rim of the mouse brain tumors. There are a few challenges with this approach. Often denoising methods applied to MR spectroscopy data have merely a cosmetic effect but the actual quantification of the peaks in the spectra is not more accurate than when applied directly to original non-denoised data. It is not clear if this concern is applicable to the denoising technique applied here. However, even if this is not an issue, no denoising method can truly increase the original spatial resolution at which data were acquired. A quick calculation estimates that the spatial resolution of the 2H MRSI used here is 30-40 times too low to capture the much smaller tumor rim volume, and therefore there is concern that normal brain tissue and tumor tissue will be the dominant metabolic signal in so-called tumor rim voxels. This means that the conclusions on metabolic features of the (much larger) tumor are much more robust than the observations attributed to the (much smaller) tumor microenvironment/tumor rim.

To achieve their goal of high-level metabolic characterization the authors set out to measure the deuterium labeling kinetics following an intravenous bolus of deuterated glucose, instead of the easier measurement of steady-state after the labeling has leveled off. These dynamic data are then used as input for a mathematical model of glucose metabolism to derive fluxes in absolute units. While this is conceptually a well-accepted approach there are concerns about the validity of the included assumptions in the metabolic model, and some of the model's equations and/or defining of fluxes, that seem different than those used by others.

Reviewer #3 (Public Review):

Summary:

Simoes et al enhanced dynamic glucose-enhanced (DGE) deuterium spectroscopy with Deuterium Metabolic Imaging (DMI) to characterize the kinetics of glucose conversion in two murine models of glioblastoma (GBM). The authors combined spectroscopic imaging and noise attenuation with histological analysis and showcased the efficacy of metabolic markers determined from DGE DMI to correlate with histological features of the tumors. This approach is also potent to differentiate the two models from GL261 and CT2A.

Strengths:

The primary strength of this study is to highlight the significance of DGE DMI in interrogating the metabolic flux from glucose. The authors focused on glutamine/glutamate and lactate. They attempted to correlate the imaging findings with in-depth histological analysis to depict the link between metabolic features and pathological characteristics such as cell density, infiltration, and distant migration.

Weaknesses:

(1) A lack of genetic interrogation is a major weakness of this study. It was unclear what underlying genetic/epigenetic aberrations in GL261 and CT2A account for the metabolic difference observed with DGE DMI. A correlative metabolic confirmation using mass spectrometry of the two tumor specimens would give insight into the observed imaging findings.

(2) A better depiction of the imaging features and tumor heterogeneity would support the authors' multimodal attempt.

(3) Integration of the various cell types in the tumor microenvironment, as allowed with the resolution of DGE DMI, will explain the observed difference between GL261 and CT2A. Is there a higher percentage of infiltrative "other cells" observed in GL261 tumor?

(4)This underlying technology with DGE DMI is capable of identifying more heterogeneous GBM tumors. A validation cohort of additional in vivo models will offer additional support to the potential clinical impact of this study.

Reviewer #1 (Public Review):

Summary:

Previous work has shown that the evolutionarily-conserved division-orienting protein LGN/Pins (vertebrates/flies) participates in division orientation across a variety of cell types, perhaps most importantly those that undergo asymmetric divisions. Micromere formation in echinoids relies on asymmetric cell division at the 16-cell stage, and these authors previously demonstrated a role for the LGN/Pins homolog AGS in that ACD process. Here they extend that work by investigating and exploiting the question of why echinoids but not other echinoderms form micromeres. Starting with a phylogenetics approach, they determine that much of the difference in ACD and micromere formation in echinoids can be attributed to differences in the AGS C-terminus, in particular a GoLoco domain (GL1) that is missing in most other echinoderms.

Strengths:

There is a lot to like about this paper. It represents a superlative match of the problem with the model system and the findings it reports are a valuable addition to the literature. It is also an impressively thorough study; the authors should be commended for using a combination of experimental approaches (and consequently generating a mountain of data).

Weaknesses:

There is an intriguing finding described in Figure 1. AGS in sea cucumbers looks identical to AGS in the pencil urchin, at least at the C terminus (including the GL1 domain). Nevertheless, there are no micromeres in sea cucumbers. Therefore another mechanism besides GL motif organization has arisen to support micromere formation. It is a consequential finding and an important consideration in interpreting the data, but I could not find any mention of it in the text. That is a missed opportunity and should be remedied, ideally not only through discussion but also experimentation. Specifically: does sea cucumber AGS (SbAGS) ever localize to the vegetal cortex in sea cucumbers? Can it do so in echinoids? Will that support micromere formation?

The authors point out that AGS-PmGL demonstrates enrichment at the vegetal cortex (arrow in 5G, quantifications in 5H), unlike PmAGS. AGS-PmGL does not however support ACD. They interpret this result to indicate "that other elements of SpAGS outside of its C-terminus can drive its vegetal cortical localization but not function." This is a critical finding and deserves more attention. Put succinctly: Vegetal cortical localization of AGS is insufficient to promote ACD, even in echinoids. Why should this be?

The authors did perform experiments to address this problem, hypothesizing that the difference might be explained by the linker region, which includes a conserved phosphorylation site that mediates binding to Dlg. They write "To test if this serine is essential for SpAGS localization, we mutated it to alanine (AGS-S389A in Fig. S3A). Compared to the Full AGS control, the mutant AGS-S389A showed reduced vegetal cortical localization (Fig. S3B-C) and function (Fig. S3D-E). Furthermore, we replaced the linker region of PmAGS with that of SpAGS (PmAGS-SpLinker in Fig. S4A-B). However, this mutant did not show any cortical localization nor proper function in ACD (Fig. S4C-F). Therefore, the SpAGS C-terminus is the primary element that drives ACD, while the linker region serves as the secondary element to help cortical localization of AGS."

The experiments performed only make sense if the AGS-PmGL chimeric protein used in Figure 5 starts the PmGL sequence only after the Sp linker, or at least after the Sp phosphorylation site. I can't tell from the paper (Figure S3 indicates that it does, whereas S5 suggests otherwise), but it's a critical piece of information for the argument. Another piece of missing information is whether the PmAGS can be phosphorylated at its own conserved phosphorylation site. The authors don't test this, which they could at least try using a phosphosite prediction algorithm, but they do show that the candidate phosphorylation site has a slightly different sequence in Pm than in Et and Sp (Fig. S4A). With impressive rigor, the authors go on to mutate the PmAGS phosphorylation site to make it identical to Sp. Nothing happens. Vegetal cortical localization does not increase over AGS-PmGL alone. Micromere formation is unrescued.

There is therefore a logic problem in the text, or at least in the way the text is written. The paragraph begins "Additionally, AGS-PmGL unexpectedly showed cortical localization (Figure 5G), while PmAGS showed no cortical localization (Figure 5B)." We want to understand why this is true, but the explanation provided in the remainder of the paragraph doesn't match the question: according to quite a bit of their own data, the phosphorylation site in the linker does not explain the difference. It might explain why AGS-PmGL fails to promote micromere formation, but only if the AGS-PmGL chimeric protein uses the Pm linker domain (see above).

Another concern that is potentially related is the measurement of cortical signal. For example, in the control panel of Figure 5C, there is certainly a substantial amount of "non-cortical" signal that I believe is nuclear. I did not see a discussion of this signal or its implications. My impression of the pictures generally is that the nuclear signal and cortical signal are inversely correlated, which makes sense if they are derived from the same pool of total protein at different points of the cell cycle. If that's the case (and it might not be) I would expect some quantifications to be impacted. For example, the authors show in Figure S3B that AGS-S389A mutant does not localize to the cortex. However, this mutant shows a radically different localization pattern to the accompanying control picture (AGS), namely strong enrichment in what I assume to be the nucleus. Is the S389 mutant preventing AGS from making it to the cortex? Or are these pictures instead temporally distinct, meaning that AGS hasn't yet made it out of the nucleus? Notably, the work of Johnston et al. (Cell 2009), cited in the text, does not show or claim that the linker domain impacts Pins localization. Their model is rather that Pins is anchored at the cortex by Gαi, not Dlg, and that is the same model described in this manuscript. In agreement with that model and the results of Johnston et al., a later study (Neville et al. EMBO Reports 2023) failed to find a role for Dlg or the conserved phosphorylation site in Pins localization.

Reviewer #2 (Public Review):

This study from Dr. Emura and colleagues addresses the relevance of AGS3 mutations in the execution of asymmetric cell divisions promoting the formation of the micromere during sea-searching development. To this aim, the authors use quantitative imaging approaches to evaluate the localisation of AGS3 mutants truncated at the N-terminal region or at the C-terminal region, and correlate these distributions with the formation of micromere and correct development of embryos to the pluteus stage. The authors also analyse the capacity of these mutated proteins to rescue developmental defects observed upon AGS3 depletion by morpholino antisense nucleotides (MO). Collectively these experiments revealed that the C-terminus of AGS3, coding for four GoLoco motifs binding to cortical Gaphai proteins, is the molecular determinant for cortical localisation of AGS3 at the micromeres and correct pluteus development. Further genetic dissections and expression of chimeric AGS3 mutants carrying shuffled copies of the GoLoco motifs or four copies of the same motifs revealed that the position of GoLoco1 is essential for AGS3 functioning. To understand whether the AGS3-GoLoco1 evolved specifically to promote asymmetric cell divisions, the authors analyse chimeric AGS3 variants in which they replaced the sea urchin GoLoco region with orthologs from other echinoids that do not form micromeres, or from Drosophila Pins or human LGN. These analyses corroborate the notion that the GoLoco1 position is crucial for asymmetric AGS3 functions. In the last part of the manuscript, the authors explore whether SpAGS3 interacts with the molecular machinery described to promote asymmetric cell division in eukaryotes, including Insc, NuMA, Par3, and Galphai, and show that all these proteins colocalize at the nascent micromere, together with the fate determinant Vasa. Collectively this evidence highlighted how evolutionarily selected AGS3 modifications are essential to sustain asymmetric divisions and specific developmental programs associated with them.

eLife assessment

This work presents valuable data demonstrating that a camelid single-domain antibody can selectively inhibit a key glycolytic enzyme in trypanosomes via an allosteric mechanism. The claim that this information can be exploited for the design of novel chemotherapeutics is incomplete and limited by the modest effects on parasite growth, as well as the lack of evidence for cellular target engagement in vivo.

Reviewer #1 (Public Review):

Summary:

The authors identified nanobodies that were specific for the trypanosomal enzyme pyruvate kinase in previous work seeking diagnostic tools. They have shown that a site involved in the allosteric regulation of the enzyme is targeted by the nanobody and using elegant structural approaches to pinpoint where binding occurs, opening the way to the design of small molecules that could also target this site.

Strengths:

The structural work shows the binding of a nanobody to a specific site on Trypanosoma congolense pyruvate kinase and provides a good explanation as to how binding inhibits enzyme activity. The authors go on to show that by expressing the nanobodies within the parasites they can get some inhibition of growth, which albeit rather weak, they provide a case on how this could point to targeting the same site with small molecules as potential trypanocidal drugs.

Weaknesses:

The impact on growth is rather marginal. Although explanations are offered on the reasons for that, including the high turnover rate of the expressed nanobody and the difficulty in achieving the high levels of inhibition of pyruvate kinase required to impact energy production sufficiently to kill parasites, this aspect of the work doesn't offer great support to developing small molecule inhibitors of the same site.

Reviewer #2 (Public Review):

Summary:

In this work, the authors show that the camelid single-chain antibody sdAb42 selectivity inhibits Trypanosome pyruvate kinase (PYK) but not human PYK. Through the determination of the crystal structure and biophysical experiments, the authors show that the nanobody binds to the inactive T-state of the enzyme, and in silico analysis shows that the binding site coincides with an allosteric hotspot, suggesting that nanobody binding may affect the enzyme active site. Binding to the T-state of the enzyme is further supported by non-linear inhibition kinetics. PYK is an important enzyme in the glycolytic pathway, and inhibition is likely to have an impact on organisms such a trypanosomes, that heavily rely on glycolysis for their energy production. The nanobody was generated against Trypanosoma congolense PYK, but for technical reasons the authors progressed to testing its impact on cell viability in Trypanosoma brucei brucei. First, they show that sdA42 is able to inhibit Tbb PYK, albeit with lower potency. Cell-based experiments next show that expression of sdA42 has a modest, and dose-dependent effect on the growth rate of Tbb. The authors conclude that their data indicates that targeting this allosteric site affects cell growth and is a valuable new option for the development of new chemotherapeutics for trypanosomatid diseases.

Strengths:

The work clearly shows that sdA42A inhibits Trypanosome and Leishmania PYK selectively, with no inhibition of the human orthologue. The crystal structure clearly identifies the binding site of the nanobody, and the accompanying analysis supports that the antibody acts as an allosteric inhibitor of PYK, by locking the enzyme in its apo state (T-state).

Weaknesses:

(1) The most impactful claim of this work is that sdAb42-mediated inhibition of PYK negatively affects parasite growth and that this presents an opportunity to develop novel chemotherapeutics for trypanosomatid diseases. For the following reasons I think this claim is not sufficiently supported:

- The authors do not provide evidence of target-engagement in cells, i.e. they do not show that sdA42A binds to, or inhibits, Tbb PYK in cells and/or do not provide a functional output consistent with PYK inhibition (e.g. effect on ATP production). Measuring the extent of target engagement and inhibition is important to draw conclusions from the modest effect on growth.

- The authors do not explore the selectivity of sdA42A in cells. Potentially sdA42A may cross-react with other proteins in cells, which would confound interpretation of the results.

- sdA42A only affects minor growth inhibition in Tbb. The growth defect is used as the main evidence to support targeting this site with chemotherapeutics, however based on the very modest effect on the parasites, one could reasonably claim that PYK is actually not a good drug target. The strongest effect on growth is seen for the high expressor clone in Figure 4a, however here the uninduced cells show an unusual profile, with a sudden increase in growth rate after 4 days, something that is not seen for any of the other control plots. This unexplained observation accentuates the growth difference between induced and uninduced, and the growth differences seen in all other experiments, including those with the highest expressors (clones 54 and 55) are much more modest. The loss of expression of sdA42A over time is presented as a reason for the limited effect, and used to further support the hypothesis that targeting the allosteric site is a suitable avenue for the development of new drugs. However, strong evidence for this is missing.

- For chemotherapeutic interventions to be possible, a ligandable site is required. There is no analysis provided of the antibody binding site to indicate that small molecule binding is indeed feasible.

(2) The authors comment on the modest growth inhibition, and refer to the need to achieve over 88% reduction in Vmax of PYK to see a strong effect, something that may or may not be achieved in the cell-based model (no target-engagement or functional readout provided). The slow binding model and switch of species are also raised as potential explanations. While these may be plausible explanations, they are not tested which leaves us with limited evidence to support targeting the allosteric site on PYK.

(3) The evidence to support an allosteric mechanism is derived from structural studies, including the in silico allosteric network predictions. Unfortunately, standard enzyme kinetics mode of inhibition studies are missing. Such studies could distinguish uncompetitive from non-competitive behaviour and strengthen the claim that sdAb42 locks the enzyme complex in the apo form.

(4) As general comment, the graphical representation of the data could be improved in line with recent recommendations: https://journals.plos.org/plosbiology/article?id=10.1371/journal.pbio.1002128, https://elifesciences.org/inside-elife/5114d8e9/webinar-report-transforming-data-visualisation-to-improve-transparency-and-reproducibility.

- Bar-charts for potency are ideally presented as dot plots, showing the individual data points, or box plots with datapoints shown.

- Images in Figure 7 show significant heterogeneity of nanobody expression, but the extent of this can not be gleaned from Figure 7B. It would be much better to use box plots or violin plots for each cell line on this figure panel. The same applies to Figure 10.

Reviewer #3 (Public Review):

Summary:

Out of the 20 Neglected Tropical Diseases (NTD) highlighted by the WHO, three are caused by members of the trypanosomatids, namely Leishmanaisis, Trypanosomiasis, and Chagas disease. Trypanosomal glycolytic enzymes including pyruvate kinase (PyK) have long been recognised as potential targets. In this important study, single-chain camelid antibodies have been developed as novel and potent inhibitors of PyK from the T, congolense. To gain structural insight into the mode of action, binding was further characterised by biophysical and structural methods, including crystal structure determination of the enzyme-nanobody complex. The results revealed a novel allosteric mechanism/pathway with significant potential for the future development of novel drugs targeting allosteric and/or cryptic binding sites.

Strengths:

This paper covers an important area of science towards the development of novel therapies for three of the Neglected Tropical Diseases. The manuscript is very clearly written with excellent graphics making it accessible to a wide readership beyond experts. Particular strengths are the wide range of experimental and computational techniques applied to an important biological problem. The use of nanobodies in all areas from biophysical binding experiments and X-ray crystallography to in-vivo studies is particularly impressive. This is likely to inspire researchers from many areas to consider the use of nanobodies in their fields.

Weaknesses:

There is no particular weakness, but I think the computational analysis of allostery, which basically relies on a single server could have been more detailed.

eLife assessment

This important study reports the molecular function of the SARS-CoV-2 helicase NSP13, which inhibits the transcriptional activity of the YAP/TEAD complex in vitro and in vivo. The evidence supporting the authors' claims is solid, with rigorous cell biological assays and multi-omic studies. This work will be of interest to scientists studying COVID-19 infection and the Hippo-YAP signaling pathway.

Reviewer #1 (Public Review):

In the manuscript entitled "SARS-CoV-2 NSP13 interacts with TEAD to suppress Hippo-YAP signaling", Meng et al. report that SARS-CoV-2 infection disrupts YAP downstream gene transcription in both patient lung samples and the iPSC-cardiomyocytes. Among the tested SARS-CoV-2 proteins, the helicase nonstructural protein 13 (NSP13) was identified to target YAP transcriptional activity both in vitro and in vivo, independent of the Hippo pathway. Mechanistically, NSP13 inhibits YAP transcriptional activity through its interaction with TEAD4 and a group of nuclear repressor proteins, a process that requires its helicase activity. Overall, this study uncovers a novel regulation of the YAP/TEAD complex by SARS-CoV-2 infection, highlighting its impact on cellular signaling events. The manuscript is well-written and easy to follow. Here are some suggestions for the authors to further improve their work.

Major points

(1) The authors discovered a novel regulation of the Hippo-YAP pathway by SARS-CoV-2 infection but did not address the pathological significance of this finding. It remains unclear why YAP downstream gene transcription needs to be inhibited in response to SARS-CoV-2 infection. Is this inhibition crucial for the innate immune response to SARS-CoV-2? The authors should re-analyze their snRNA-seq and bulk RNA-seq data described in Figure 1 to determine whether any of the affected YAP downstream genes are involved in this process.

(2) The authors concluded that helicase activity is required for NSP13-induced inhibition of YAP transcriptional activity based on mutation studies (Figure 3B). This finding is somewhat confusing, as K131, K345/K347, and R567 are all essential residues for NSP13 helicase activity while mutating K131 did not affect NSP13's ability to inhibit YAP (Figure 3B). Additionally, there are no data showing exactly how NSP13 inhibits the YAP/TEAD complex through its helicase function. This point was also not reflected in their proposed working model (Figure 4H).

(3) The proposed model that NSP13 binds TEAD4 to recruit repressor proteins and inhibits YAP/TEAD downstream gene transcription (Figure 4H) needs further characterization. First, it is notable that the provided NSP13 IP-MS data did not reveal any TEAD family members as binding proteins for NSP13 (Supplement Figure 4C and the tables), suggesting that NSP13 may modulate the YAP/TEAD complex through other mechanisms, possibly involving other binding proteins. Second, NSP13 is a DNA-binding protein, and its nucleic acid-binding mutant K345A/K347A failed to inhibit YAP transcriptional activity (Figure 3B). The authors should investigate whether NSP13 could bind to the TEAD binding sequence or the nearby sequence on the genome to modulate TEAD's DNA binding ability. Third, regarding the identified nuclear repressors, the authors should validate the interaction of NSP13 with the ones whose loss activates YAP transcriptional activity (Figure 4G). Lastly, why can't NSP13 bind TEAD4 in the cytoplasmic fractionation if both NSP13 and TEAD4 are detected there (Figure 3B)? This finding indicates their interaction is not a direct protein-protein interaction but is mediated by something in the nucleus, such as genomic DNA.

Reviewer #2 (Public Review):

Summary:

The manuscript by Meng et al. describes a potential role for the coronavirus helicase NSP13 in the regulation of YAP-TEAD activity. The authors present data that NSP13 expression in cells reduces YAP-induced TEAD luciferase reporter activity and that NSP13 transduction in cardiomyocytes blocks hyperactive YAP-mutant phenotypes in vivo. Mechanisms by which viral proteins (particularly those from coronavirus) intersect with cellular signaling events is an important research topic, and the intersection of NSP13 with YAP-TEAD transcriptional activity (independent of upstream Hippo pathway mediated signals) offers new knowledge that is of interest to a broad range of researchers.

Strengths:

The manuscript presents convincing data mapping the effects of NSP13 on YAP-TEAD reporter activity in the helicase domain. Moreover, the in vivo data demonstrating that NSP13 expression in YAP5SA mouse cardiomyocytes increased survival animal rates, and restored cardiac function is striking and is supportive of the model presented.

Weaknesses:

Limitations to the study are the reliance on TEAD-reporter assays to show specific effects of NPS13 on YAP-TEAD activity, incomplete characterization of the interesting in vivo findings that are presented, and a lack of follow-up to the proposed mechanisms identified from the IP-MS experiments.

Specific comments and suggestions for improvement of the manuscript:

(1) NSP13 has been reported to block, in a helicase-dependent manner, episomal DNA transcription (PMID: 37347173), raising questions about the effects observed on the data shown from the HOP-Flash and 8xGTIIC assays. It would be valuable to demonstrate the specificity of the proposed effect of NSP13 on TEAD activation by YAP (versus broad effects on reporter assays) and also to show that NSP13 reduces the function of endogenous YAP-TEAD transcriptional activity (i.e., does ectopic NSP13 expression reduce the expression of YAP induced TEAD target genes in cells).

(2) While the IP-MS experiment may have revealed new regulators of TEAD activity, the data presented are preliminary and inconclusive. No interactions are validated and beyond slight changes in TEAD reporter activity following knockdown, no direct links to YAP-TEAD are demonstrated, and no link to NPS13 was shown. Also, no details are provided about the methods used for the IP-MS experiment, raising some concerns about potential false positive associations within the data.

Author response:

Reviewer #1 (Recommendations For The Authors):

(1) Figure 3B was not cited in the manuscript.

We have now included the citation for Figure 3B in the main text: “….whereas NSP13-R567A (lost ATP consumption) and NSP13-K345A/K347A (obstructed the nucleic acid binding channel) failed to inhibit YAP activity (Figure 3B).” (Please see the revised manuscript) 

Reviewer #2 (Recommendations For The Authors):

(2) In Figure 1, ciliated cells are marked as a separate cluster from "epithelial cells". Since ciliated cells are epithelial cells, I suggest changing the nomenclature of the clusters.

We have updated the label from “Ciliated” to “Ciliated Epithelial” in Figure 1A, as suggested. (Please see the revised manuscript)

(3) Outlines of planned revisions: 1) Reanalyze snRNA-seq and bulk RNA-seq data from Figure 1 to investigate YAP target genes related to innate immune response; 2) Employ ChIP-seq to determine whether NSP13 WT or mutants (K131, K345/K347, and R567) prevent YAP/TEAD complex from binding to DNA by occupying the TEAD DNA binding site, providing insights into the mechanism; 3) Validate NSP13 interacting proteins using Immunoprecipitation-Western Blot (IP-WB) assays based on mass spectrum results; 4) Perform bulk RNA sequencing in cells with or without NSP13 expression to assess endogenous YAP target genes expression.

Author response:

The following is the authors’ response to the current reviews.

Reviewer #1 (Public Review):

Overall the authors provide a very limited data set and in fact only a proof of concept that their sensor can be applied in vivo. This is not really a research paper, but a technical note. With respect to their observation of clustered activity, they now provide an overview image, next to zoomed details. However, from these images one cannot conclude 'by eye' any clustering event. This aligns with the very low r values. All neurons in the field show variable activity and a clustering is not really evident from these examples. Even within a cluster, there is variability. The authors now confirm that expression levels are indeed variable but are independent from the ratio measurements. Further, they controlled for specificity by including DAPT treatments, but opposite to their own in vitro data (in primary neurons) the ratios increased. The authors argue that both distance and orientation can either decrease or increase ratios and that the use of this biosensor should be explored model-by-model. This doesn't really confer high confidence and may hinder other groups in using this sensor reliably.

Secondly, there is still no physiological relevance for this observation. The experiments are performed in wild-type mice, but it would be more relevant to compare this with a fadPSEN1 KI or a PSEN1cKO model to investigate the contribution of a gain of toxic function or LOF to the claimed cell non-autonomous activations. The authors acknowledge this shortcoming but argue that this is for a follow-up study.

For instance, they only monitor activity in cell bodies, and miss all info on g-sec activity in neurites and synapses: what is the relevance of the cell body associated g-sec and can it be used as a proxy for neuronal g-sec activity? If cells 'communicate' g-sec activities, I would expect to see hot spots of activity at synapses between neurons.

Without some more validation and physiologically relevant studies, it remains a single observation and rather a technical note paper, instead of a true research paper.

The effect size was small, as stated in the original and revised manuscripts and the point-by-point responses to the 1st round review. Such subtle effects will likely be challenging to detect by eye. However, our unbiased quantification allowed us to detect a statistically significant linear correlation between the 720/670 ratio in each neuron and the average ratio in neighboring neurons, which we have verified using many different approaches (Figure 3, Figure 3—figure supplement 2, and Figure 4), and the correlation was canceled by the administration of g-secretase inhibitor (Figure 5). Such objective analysis made us more confident to conclude that g-secretase affects g-secretase in neighboring neurons.

We would also like to make clear the design of the C99 720-670 biosensor. Both C99, the sensing domain that is cleaved by g-secretase, and the anchoring domain fused to miRFP670 are integrated into the membrane (Figure 1A). Therefore, how these two domains with four transmembrane regions are embedded in the membrane should affect the orientation between the donor, miRFP670, and the acceptor, miRFP720. As noted in our point-by-point responses to the initial review, we have previously validated that pharmacological inhibition of g-secretase significantly increases the FRET ratio in various cell lines, including CHO, MEF, BV2 cells, and mouse cortical primary neurons (Maesako et al., 2020; Houser et al., 2020, and unpublished observations). On the other hand, FRET reduction by g-secretase inhibition was found in mouse primary neurons derived from the cerebellum (unpublished observations) as well as the somatosensory cortex neurons in vivo (this study). While we could not use the exact same imaging set-up between cortical primary neurons in vitro and those in vivo due to different expression levels of the biosensor, we could do it for in vitro cortical primary neurons vs. in vitro cerebellum neurons. We found by the direct comparison that 720/670 ratios are significantly higher in the cerebellum than the cortex neurons even in the presence of 1 mM DAPT (Author response image 1), a concentration that nearly completely inhibits g-secretase activity. This suggests a different integration and stabilization pattern of the sensing and anchoring domains in the C99 720-670 biosensor between the cortex and cerebellum primary neurons, and thus, orientation between the donor and acceptor varies in the two neuronal types. We expect a similar scenario between cortical primary neurons in vitro and those in vivo. Of note, we have recently demonstrated that the cortex and cerebellum primary neurons exhibit distinct membrane properties (Lundin and Wieckiewicz et al., 2024 in revision), suggesting the different baseline FRET could be related to the different membrane properties between the cortex and cerebellum primary neurons. On the other hand, this raises a concern that 720/670 ratios can be affected not only by g-secretase activity but also by other cofounders, such as altered membrane properties. However, a small but significant correlation between the 720/670 ratio in a neuron and those ratios in its neighboring neurons is canceled by g-secretase inhibitor (Figure 5), suggesting that the correlation between the 720/670 ratio in a neuron and those in its neighboring neurons is most likely dependent on g-secretase activity. Taken together, we currently think orientation plays a significant role in our biosensor and would like to emphasize the importance of ensuring on a model-by-model basis whether the cleavage of the C99 720-670 biosensor by g-secretase increases or decreases 720/670 FRET ratios.

Author response image 1.

Furthermore, we co-expressed the C99 720-670 biosensor and visible range fluorescence reporters to record other biological events, such as changes in ion concentration, in cortex primary neurons. Interestingly, several biological events uniquely detected in the neurons with higher 720/670 ratios, which are expected to exhibit lower endogenous g-secretase activity, are recapitulated by pharmacological inhibition of g-secretase (unpublished observations), ensuring that higher 720/670 ratios are indicative of lower g-secretase activity in mouse cortex primary neurons. Such multiplexed imaging will help to further elucidate how the C99 720-670 biosensor behaves in response to the modulation of g-secretase activity.

Lastly, the scope of this study was to develop and validate a novel imaging assay employing a NIR FRET biosensor to measure g-secretase activity on a cell-by-cell basis in live wild-type mouse brains. However, we do appreciate the reviewer’s suggestion and think employing this new platform in FAD PSEN1 knock-in (KI) or PSEN1 conditional knockout (cKO) mice would provide valuable information. Furthermore, we are keen to expand our capability to monitor g-secretase with subcellular resolution in live mouse brains in vivo, which we will explore in follow-up studies. Thank you for your thoughtful suggestions.

Reference

- Maesako M, Sekula NM, Aristarkhova A, Feschenko P, Anderson LC, Berezovska O. Visualization of PS/γ-Secretase Activity in Living Cells. iScience. 2020 Jun 26;23(6):101139.

- Houser MC, Hou SS, Perrin F, Turchyna Y, Bacskai BJ, Berezovska O, Maesako M. A Novel NIR-FRET Biosensor for Reporting PS/γ-Secretase Activity in Live Cells. Sensors (Basel). 2020 Oct 22;20(21):5980.

- Lundin B, Wieckiewicz N, Dickson JR, Sobolewski RGR, Sadek M, Armagan G, Perrin F, Hyman BT, Berezovska O, and Maesako M. APP is a regulator of endo-lysosomal membrane permeability. 2024 in revision

Reviewer #2 (Public Review):

Regarding the variability and spatial correlation- the dynamic range of the sensor previously reported in vitro is in the range of 20-30% change (Houser et al 2020) whereas the range of FR detected in vivo is between cells is significantly larger in this MS. This raises considerable doubts for specific detection of cellular activity.

One direct way to test the dynamic range of the sensor in vivo, is to increase or decrease endogenous gamma-secretase activity and to ensure this experimental design allows to accurately monitor gamma-secretase activity. In the previous characterization of the reporter (Hauser et al 2020), DAPT application and inhibition of gamma-secretase activity results in increased FR (Figures 2 and 3 of Houser et al). This is in agreement with the design of the biosensor, since FR should be inversely correlated with enzymatic activity. Here, the authors repeated the experiment, and surprisingly found an opposite effect, in which DAPT significantly reduced FR.

The authors maintain that this result could be due to differences in cell-types, However, this experiment was previously performed in cultures cortical neurons and many different cell types, as noted by the authors in their rebuttal.

Instead, I would argue that these results further highlight the concerns of using FR in vivo, since based on their own data, there is no way to interpret this quantification. If DAPT reduces FR, does this mean we should now interpret the results of higher FR corresponds to higher g-sec activity? Given a number of papers from the authors claiming otherwise, I do not understand how one can interpret the results as indicating a cell-specific effect.

In conclusion, without any ground truth, it is impossible to assess and interpret what FR measurements of this sensor in vivo mean. Therefore, the use of this approach as a way to study g-sec activity in vivo seems premature.

Please find our response to reviewer 1’s similar critique above. Here, we again would like to re-clarify the design of our C99 720-670 biosensor. The orientation between the donor, miRFP670, and acceptor, miRFP720, is dependent on how C99, the sensing domain that is cleaved by g-secretase, and the anchoring domain are integrated into the membrane (Figure 1A). Although it was surprising to us, it is possible that g-secretase inhibition decreases 720/670 ratios if 1) the donor-acceptor orientation plays a significant role in FRET and 2) the baseline structure of the C99 720-670 biosensor is different between cell types. This appears to be the case between the cortex and cerebellum primary neurons (i.e., DAPT increases 720/670 ratios in the cortex neurons while decreasing in the cerebellum neurons), and we expect it in cortical neurons in vitro vs. in vivo as well. Hence, we recommend that users first validate whether the cleavage of the C99 720-670 biosensor by g-secretase increases or decreases 720/670 FRET ratios in their models. If DAPT increases 720/670 ratios (like in cortex primary neurons, CHO, MEF, and BV2 cells that we have validated), the results of higher ratios should be interpreted as lower g-secretase activity. If DAPT reduces 720/670 ratios (like in cerebellum primary neurons and the somatosensory cortex neurons in vivo), we should interpret the results of higher ratios corresponding to higher g-secretase activity. From a biosensing perspective, although we need to know which is the case on a model-by-model basis, we think whether g-secretase activity increases or decreases the 720/670 ratio is not critical; rather, if it can significantly change FRET efficiency is more important. Thank you for your critical comments.

Reviewer #3 (Public Review):

This paper builds on the authors' original development of a near infrared (NIR) FRET sensor by reporting in vivo real-time measurements for gamma-secretase activity in the mouse cortex. The in vivo application of the sensor using state-of-the-art techniques is supported by a clear description and straightforward data, and the project represents significant progress because so few biosensors work in vivo. Notably, the NIR biosensor is detectable to ~ 100 µm depth in the cortex. A minor limitation is that this sensor has a relatively modest ΔF as reported in Houser et al, which is an additional challenge for its use in vivo. Thus, the data is fully dependent on post-capture processing and computational analyses. This can unintentionally introduce biases but is not an insurmountable issue with the proper controls that the authors have performed here.

The following opportunity for improving the system didn't initially present itself until the authors performed an important test of the FRET sensor in vivo following DAPT treatment. The authors get credit for diligently reporting the unexpected decrease in 720/670 FRET ratio. In turn this has led to a suggestion that this sensor would benefit from a control that is insensitive to gamma-secretase activity. FRET influences that are independent of gamma-secretase activity could be distinguished by this control.

From previous results in cultured neurons, the authors expected an increase in FRET following DAPT treatment in vivo. These expectations fit with the sensor's mode-of-action because a block of gamma-secretase activity should retain the fluorophores in proximity. When the authors observed decreased FRET, the conclusion was that the sensor performs differently in different cellular contexts. However, a major concern is that mechanistically it is unclear how this could occur with this type of sensor. The relative orientation of fluorophores indeed can contribute to FRET efficiency in tension-based sensors. However, the proteolysis expected with gamma-secretase activity would release tension and orientation constraints. Thus, the major contributing FRET factor is expected to be distance, not orientation. Alternative possibilities that could inadvertently affect readouts include an additional DAPT target in vivo sequestering the inhibitor, secondary pH effects on FRET, photo-bleaching, or an unidentified fluorophore quencher in vivo stimulated by DAPT. Ultimately this new FRET sensor would benefit from a control that is insensitive to gamma-secretase activity. FRET influences that are independent of gamma-secretase activity could be distinguished by this control.

Given that the anchoring domain is composed of three transmembrane regions and the linker connecting the donor, miRFP670, and the acceptor, miRFP720, is highly flexibility, we are still not sure if the orientation constraint of the C99 720-670 biosensor is canceled by g-secretase cleavage. This means that the orientation between the donor and acceptor in the cleaved form of the sensor can be different between model and model. As explained in response to the similar critique of reviewer 1, we found that the 720/670 ratio is significantly higher in the cerebellum than in the cortex neurons even in the presence of DAPT (Figure 1 for the review only). Therefore, we currently think the donor-acceptor orientation, both in the cleaved and non-cleaved forms of the sensor, plays a role in determining whether g-secretase activity increases or decreases the 720/670 ratio (but this view may change depends on the future discoveries).

As the reviewer pointed out, the NIR g-secretase biosensor with no biological activity is important; however, a point mutation in the transmembrane region of the C99 sensing domain could also result in altered orientation between the donor, miRFP670, and the acceptor, miRFP720, since C99 is connected to the acceptor, which may bring additional complexity. Also, as noted in our point-by-point responses to the initial review, the mutation(s) that can fully block C99 processing by g-secretase has not been established. Therefore, we asked if a subtle but significant correlation we found between the 720/670 ratio in a neuron and those ratios in its neighboring neurons is canceled by g-secretase inhibitor administration. Since the correlation was abolished (Figure 5), it suggests that the correlation between the 720/670 ratio in a neuron and those ratios in the neighboring neurons depends on g-secretase activity.

It is not fully established how g-secretase activity is spatiotemporally regulated; therefore, the development of more appropriate control biosensors and further validation of our findings with complementary approaches would be crucial in our follow-up studies. Thank you for your valuable comments.

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The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

(1) Overall the authors provide a very limited data set and in fact only a proof of concept that their sensor can be applied in vivo. This is not really a research paper, but a technical note. With respect to their observation of clustered activity, the images do not convince me as they show only limited areas of interest: from these examples (for instance fig 5) one sees that merely all neurons in the field show variable activity and a clustering is not really evident from these examples. Even within a cluster, there is variability. With r values between 0.23 to .36, the correlation is not that striking. The authors herein do not control for expression levels of the sensor: for instance, can they show that in all neurons in the field, the sensor is equally expressed, but FRET activity is correlated in sets of neurons? Or are the FRET activities that are measured only in positively transduced neurons, while neighboring neurons are not expressing the sensor? Without such validation, it is difficult to make this conclusion.

We appreciate the reviewer’s comment. We agree with the reviewer that this study is not testing a new hypothesis but rather developing and validating a novel tool. However, we do believe such a “technical note” is as important as a “research paper” since advancing technique(s) is the only way to break the barrier in our understanding of complex biological events. Therefore, this study aimed to develop and validate a novel imaging assay employing a recently engineered NIR FRET biosensor to measure γ-secretase activity (Houser et al., 2020) on a cell-by-cell basis in live mouse brains, enabling us for the first time to examine how γ-secretase activity is regulated in individual neurons in vivo, and uncover that γ-secretase activity may influence γ-secretase in neighboring neurons. Like the reviewer, we found that the cell-to-cell correlation is not that striking, as we clearly stated in the original manuscript: “Although the effect size is modest, we also found a statistically significant correlation between…” 

We were also aware that there is variability in a cluster of neurons exhibiting similar γ-secretase activities. Per the reviewer’s request, the images have been expanded to the entire imaging field of view (new Figure 3A). Although the effect size is small, our unbiased quantification showed a statistically significant linear correlation between the 720/670 ratio in each neuron and the average ratio in five neighboring neurons (Figure 3, Figure 3—figure supplement 2, and Figure 4), and the correlation was canceled by the administration of γ-secretase inhibitor (Figure 5). These findings made it impossible to conclude that γ-secretase does not affect γ-secretase in neighboring neurons.

Regarding the expression levels and pattern of the sensor, an AAV-based gene delivery approach employed in this study results in the expression of the sensor not in all but in selected neurons. We have newly performed immunohistochemistry, showing that approximately 40% of NeuN-positive neurons express the C99 720-670 biosensor (new Figure 1—figure supplement 2A and 2B).

Reference

- Houser MC, Hou SS, Perrin F, Turchyna Y, Bacskai BJ, Berezovska O, Maesako M. A Novel NIRFRET Biosensor for Reporting PS/γ-Secretase Activity in Live Cells. Sensors (Basel). 2020 Oct 22;20(21):5980. 

(2) Secondly, I am lacking some more physiological relevance for this observation. The experiments are performed in wild-type mice, but it would be more relevant to compare this with a fadPSEN1 KI or a PSEN1cKO model to investigate the contribution of a gain of toxic function or LOF to the claimed cell non-autonomous activations. Or what would be the outcome if the sensor was targeted to glial cells?

The AAV vector in this study encodes the human synapsin promoter and our new immunohistochemistry demonstrates that nearly 100% of the cells expressing the C99 720-670 sensor are NeuN positive, and we hardly detected the sensor expression in Iba-1 or GFAP-positive cells (new Figure 1— figure supplement 2A and 2C). 

The mechanism underlying the cell non-autonomous regulation of γ-secretase remains unclear. As discussed in our manuscript, one of the potential hypotheses could be that secreted abeta42 plays a role (Zoltowska et al., 2023 eLife). Whereas this report focuses on the development and validation of a novel assay using wildtype mice, future follow-up studies employing FAD PSEN1 knock-in (KI) and PSEN1 conditional knockout (cKO) mice would allow us test the hypothesis above since abeta42 is known to increase in some FAD PSEN1 KI mice (Siman et al., 2000 J Neurosci, Vidal et al., 2012 FASEB J) while decreases in PSEN1 cKO mice (Yu et al., 2001 Neuron).  

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(3) For this reviewer it is not clear what resolution they are measuring activity, at cellular or subcellular level? In other words are the intensity spots neuronal cell bodies? Given g-sec activity are in all endosomal compartments and at the cell surface, including in the synapse, does NIR imaging have the resolution to distinguish subcellular or surface localized activities? If cells 'communicate' g-sec activities, I would expect to see hot spots of activity at synapses between neurons: is this possible to assess with the current setup? 

Since this study aimed to determine how γ-secretase activity is regulated on a cell-by-cell basis in live mouse brains, the FRET signal was detected in neuronal cell bodies. While our current set-up for in vivo can only record γ-secretase activity with a cellular resolution, we previously detected predominant γ-secretase activity in the endo-lysosomal compartments (Maesako et al., 2022 J Neurosci) as well as in certain spots of neuronal processes (Maesako et al., 2020 iScience) in cultured primary neurons using the same microscope set-up. Therefore, future studies will expand our capability to monitor γ-secretase with subcellular resolution in live mouse brains in vivo.

Reference

- Maesako M, Sekula NM, Aristarkhova A, Feschenko P, Anderson LC, Berezovska O. Visualization of PS/γ-Secretase Activity in Living Cells. iScience. 2020 Jun 26;23(6):101139. 

- Maesako M, Houser MCQ, Turchyna Y, Wolfe MS, Berezovska O. Presenilin/γ-Secretase Activity Is Located in Acidic Compartments of Live Neurons. J Neurosci. 2022 Jan 5;42(1):145-154. 

(4) Without some more validation and physiological relevant studies, it remains a single observation and rather a technical note paper, instead of a true research paper.

Please find our response above to the critique (1).  

Reviewer #2 (Public Review):

(1) Regarding the variability and spatial correlation- the dynamic range of the sensor previously reported in vitro is in the range of 20-30% change (Houser et al 2020) whereas the range of FR detected in vivo is between cells is significantly larger (Fig. 3). This raises considerable doubts for specific detection of cellular activity (see point 3).

Please find our response below to the critique (2).

(2) One direct way to test the dynamic range of the sensor in vivo, is to increase or decrease endogenous gamma-secretase activity and to ensure this experimental design allows to accurately monitor gamma-secretase activity. In the previous characterization of the reporter (Hauser et al 2020), DAPT application and inhibition of gammasecretase activity results in increased FR (Figures 2 and 3 of Houser et al). This is in agreement with the design of the biosensor, since FR should be inversely correlated with enzymatic activity. Here, while the authors repeat the same manipulation and apply DAPT to block gamma-secretase activity, it seems to induce the opposite effect and reduces FR (comparing figures 8 with figures 5,6,7). First, there is no quantification comparing FR with and without DAPT. Moreover, it is possible to conduct this experiment in the same animals, meaning comparing FR before and after DAPT in the same mouse and cell populations. This point is absolutely critical- if indeed FR is reduced following DAPT application, this needs to be explained since this contradicts the basic design and interpretation of the biosensor.

We appreciate the reviewer’s comment. In our hand, overexpression of γ-secretase four components (PSEN, Nct, Aph1, and Pen2) is the only reliable and reproducible approach to increase the cellular activity of γ-secretase, which we successfully employed in vitro but not in vivo yet. Therefore, a γ-secretase inhibitor was used to determine the dynamic range of our FRET biosensor in vivo. FRET efficiency depends on the proximity and orientation of donor and acceptor fluorescent proteins. In our initial study, we engineered the original C99 EGFP-RFP biosensor (C99 R-G), and the replacement of EGFP and RFP with mTurquoise-GL and YPet, respectively, expanded the dynamic range of the sensor approximately 2 times. Moreover, extending the linker length from 20 a.a. to 80 a.a. increased the dynamic range 2.2 times (Maesako et al., 2020 iScience). Of note, the C99 720-670 NIR analog, which has the same 80 a.a. linker but miRFP670 and miRFP720 as the donor and acceptor, exhibited a slightly better dynamic range than the C99 Y-T sensor (Houser et al., 2020 Sensor). Our interpretation, at that time, was that the cleavage of the C99 720-670 biosensor by γ-secretase results in a longer distance between the donor and acceptor, and thus, the FRET ratio always increases by γ-secretase inhibition (i.e., proximity plays a more significant role than orientation in our biosensors). As expected, a significantly increased FRET ratio was detected in various cell lines by γ-secretase inhibitors, including CHO, MEF, BV2 cells, and mouse cortical primary neurons. Moreover, to further ensure the C99 720-670 biosensor records changes in γ-secretase activity, the multiplexing capability of the biosensor was utilized. In other words, we co-expressed the C99 720-670 biosensor and visible range fluorescence reporters to record other biological events, such as changes in ion concentration, etc., in cortex primary neurons. Strikingly, several biological events uniquely detected in the neurons with diminished endogenous γ-secretase activity, i.e., neurons with higher FRET ratios, are recapitulated by pharmacological inhibition of γ-secretase (unpublished observation). This approach has allowed us to ensure that increased FRET ratios are indicative of decreased endogenous γ-secretase activity in mouse cortical primary neurons. 

However, as recommended by the reviewer, we have performed a new experiment to compare the FRET ratio before and after DAPT, a potent γ-secretase inhibitor, administration in the same mouse and cell populations. Surprisingly, we found that of DAPT significantly decreases 720/670 ratios, which is included in our revised manuscript (Figure 2—figure supplement 2C). This unexpected FRET reduction by γ-secretase inhibition was also found in mouse primary neurons derived from the cerebellum (unpublished observation). These findings suggest that orientation plays a significant role in our γ-secretase FRET biosensor and whether the FRET ratio is increased or decreased by the γ-secretase-mediated cleavage depends on cell types. Of note, the difference in FRET ratios with and without DAPT was comparable between primary cortex neurons (24.3%) and the somatosensory cortex neurons in vivo (22.1%). Our new findings suggest that how our biosensors report γ-secretase activity (i.e., increased vs. decreased FRET ratio) must be examined on a model-by-model basis, which is clearly noted in the revised manuscript: 

Reference

- Houser MC, Hou SS, Perrin F, Turchyna Y, Bacskai BJ, Berezovska O, Maesako M. A Novel NIRFRET Biosensor for Reporting PS/γ-Secretase Activity in Live Cells. Sensors (Basel). 2020 Oct 22;20(21):5980. 

- Maesako M, Sekula NM, Aristarkhova A, Feschenko P, Anderson LC, Berezovska O. Visualization of PS/γ-Secretase Activity in Living Cells. iScience. 2020 Jun 26;23(6):101139. 

(3) For further validation, I would suggest including in vivo measurements with a sensor version with no biological activity as a negative control, for example, a mutation that prevents enzymatic cleavage and FRET changes. This should be used to showcase instrumental variability and would help to validate the variability of FR is indeed biological in origin. This would significantly strengthen the claims regarding spatial correlation within population of cells.

We fully agree with the reviewer that having a sensor version containing a mutation, which prevents enzymatic cleavage and thus FRET changes, as a negative control is preferable. In our previous study, we developed and validated the APP-based C99 Y-T and Notch1-based N100 Y-T biosensors (Maesako et al., 2020 iScience). It is well established that Notch1 cleavage is entirely blocked by Notch1 V1744G mutation (Schroeter et al., 1998 Nature; Huppert et al., 2000 Nature), and therefore, we introduced the mutation into N100 Y-T biosensor and used it as a negative control. On the other hand, such a striking mutation has never been identified in APP processing. To successfully monitor γ-secretase activity in deep tissue in vivo, we replaced Turquoise-GL and YPet in the C99 Y-T and N100 Y-T biosensors with miRFP670 and miRFP720, respectively. While the APP-based C99 720-670 biosensor allows recording γ-secretase activity (Houser et al., 2020 Sensors), we found the N100 720-670 sensor exhibits a very small dynamic range, not enabling to reliably measure γ-secretase activity. Taken together, there is not currently available NIR γ-secretase biosensor with no biological activity.

Reference

- Houser MC, Hou SS, Perrin F, Turchyna Y, Bacskai BJ, Berezovska O, Maesako M. A Novel NIRFRET Biosensor for Reporting PS/γ-Secretase Activity in Live Cells. Sensors (Basel). 2020 Oct 22;20(21):5980. 

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- Maesako M, Sekula NM, Aristarkhova A, Feschenko P, Anderson LC, Berezovska O. Visualization of PS/γ-Secretase Activity in Living Cells. iScience. 2020 Jun 26;23(6):101139. 

- Schroeter EH, Kisslinger JA, Kopan R. Notch-1 signalling requires ligand-induced proteolytic release of intracellular domain. Nature. 1998 May 28;393(6683):382-6. 

(4) In general, confocal microcopy is not ideal for in vivo imaging. Although the authors demonstrate data collected using IR imaging increases penetration depth, out of focus fluorescence is still evident (Figure 4). Many previous papers have primarily used FLIM based analysis in combination with 2p microscopy for in vivo FRET imaging (Some examples: Ma et al, Neuron, 2018; Massengil et al, Nature methods, 2022; DIaz-Garcia et al, Cell Metabolism, 2017; Laviv et al, Neuron, 2020). This technique does not rely on absolute photon number and therefore has several advantage sin terms of quantification of FRET signals in vivo.

It is therefore likely that use of previously developed sensors of gamma-secretase with conventional FRET pairs, might be better suited for in vivo imaging. This point should be at least discussed as an alternative.

The reviewer notes that 2p-FLIM may provide certain advantages over our confocal spectral imaging approach for detecting in vivo FRET. In our response below, we will address both the FRET detection method (FLIM vs. spectral) and microscope modality (2p vs. confocal). 

As noted by the reviewer, we do acknowledge that 2p-FLIM has been utilized to detect FRET in vivo. On the other hand, the ratiometric spectral FRET approach has also been utilized in many in vivo FRET studies (Kuchibhotla et al., 2008 Neuron; Kuchibhotla et al., 2014 PNAS; Hiratsuka et al., 2015 eLife; Maesako et al., 2017 eLife; Konagaya et al., 2017 Cell Rep; Calvo-Rodriguez et al., 2020 Nat Communi; Hino et al., 2022 Dev Cell). We think both approaches have advantages and disadvantages, as discussed in a previous review (Bajar et al., 2016 Sensors), but they complement each other. Indeed, we regularly employ FLIM in cell culture studies (Maesako et al., 2017 eLife; McKendell et al., 2022 Biosensors; Devkota 2024 Cell Rep), and our recent study also utilized 2p-FLIM for in vivo NIR imaging (although not for detecting FRET) (Hou et al., 2023, Nat Biomed Eng); therefore, we are confident that 2p-FLIM can be adapted in our follow-up studies for γ-secretase recording.

Regarding microscope modality, we agree with the reviewer’s point that generally two-photon microscopy can achieve larger penetration depths than confocal microscopy and is therefore more ideal for in vivo FRET imaging. However, in this study, since our aim was to quantify γ-secretase activity in the superficial layers of the cortex (<200 microns in depth), both NIR confocal and multiphoton microscopies could be used to achieve this imaging objective. Additionally, we chose to use confocal microscopy with our NIR C99 720-670 probe due to the probe’s slightly but higher sensitivity compared to our C99 Y-T probe (Houser et al., 2020 Sensors). Imaging γ-secretase activity with our NIR C99-720-670 probe has the additional advantage that it will allow us in future studies to multiplex with visible FRET pairs using multiphoton microscopy in the same brain region. Furthermore, our demonstration of in vivo FRET imaging using NIR confocal microscopy avoids some of the issues associated with multiphoton microscopy, including potential phototoxicity due to high average and peak laser powers and the high complexity and costs of the instrumentation. For future studies aimed at interrogating γ-secretase activity in deeper cortical regions, multiphoton microscopy could be applied for FLIM or ratiometric spectral imaging of either our NIR or visible FRET probes. Per the reviewer’s request, we have added multiphoton FRET imaging as an alternative in the discussion section. 

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(Recommendations For The Authors):

(5) Minor issues- Figure 4 describes the analysis procedure, which seems to be standard practice in the field. This can be described in the methods section rather than in the main figure.

Per the reviewer’s suggestion, this figure has been moved to Figure 2—figure supplement 1. 

Reviewer #3 (Public Review):

(1) This paper builds on the authors' original development of a near infrared (NIR) FRET sensor by reporting in vivo real-time measurements for gamma-secretase activity in the mouse cortex. The in vivo application of the sensor using state of the art techniques is supported by a clear description and straightforward data, and the project represents significant progress because so few biosensors work in vivo. Notably, the NIR biosensor is detectable to ~ 100 µm depth in the cortex. A minor limitation is that this sensor has a relatively modest ΔF as reported in Houser et al, which is an additional challenge for its use in vivo. Thus, the data is fully dependent on post-capture processing and computational analyses. This can unintentionally introduce biases but is not an insurmountable issue with the proper controls that the authors have performed here.

We appreciate the reviewer’s overall positive evaluation. As described in our response to the Reviewer 2’s critique (2), ΔF in vivo has been characterized (Figure 2—figure supplement 2C).

(2) The observation of gamma-secretase signaling that spreads across cells is potentially quite interesting, but it can be better supported. An alternative interpretation is that there exist pre-formed and clustered hubs of high gamma-secretase activity, and that DAPT has stochastic or differential accessibility to cells within the cluster. This could be resolved by an experiment of induction, for example, if gamma-secretase activity is induced or activated at a specific locale and there was observed coordinated spreading to neighboring neurons with their sensor.

We agree with the reviewer that the stochastic or differential accessibility of DAPT to cell clusters with different γ-secretase can be an alternative interpretation of our data, which is now included in the Discussion of the revised manuscript. Undoubtedly, the activation of γ-secretase would provide valuable information. However, as described in the response above to Reviewer 2’s critique #2, overexpressing the four components of γ-secretase (PSEN, Nct, Aph1, and Pen2) is the only reliable and reproducible approach to increasing the cellular activity of γ-secretase, which was achieved in our in vitro study but not yet in vivo. Our future study will develop and characterize the approach to induce γ-secretase activity to further perform detailed mechanistic studies.

(3) Furthermore, to rule out the possibility that uneven viral transduction was not simply responsible for the observed clustering, it would be helpful to see an analysis of 670nm fluorescence alone.

Our new analysis comparing 670 nm fluorescence intensity and that in five neighbor neurons shows a positive correlation (Figure 3—figure supplement 1A), suggesting that AAV was unevenly transduced. On the other hand, the 720/670 ratio (i.e., γ-secretase activity) is not correlated with 670 nm fluorescence intensity (i.e., C99 720-670 biosensor expression) (Figure 3—figure supplement 1B). This strongly suggests that, while C99 720-670 biosensor expression was not evenly distributed in the brain, the uneven probe expression did not impact the capability of γ-secretase recording.  

Reviewer #3 (Recommendations For The Authors):

(4) One minor suggestion might be to consider Figures 6-7 as orthogonal supporting analyses rather than "validation". It might then be helpful to present them together with Figure 5.

We have moved the initial Figure 6 and 7 to Figure 3—figure supplement 2 and Figure 4, respectively.

eLife assessment

Hou and colleagues describe the the use of a previously characterized FRET sensor for use in determining gamma secretase activity in the brain of living mice. In an approach that targeted the sensor to neurons, they observe patterns of fluorescent sensor readout suggesting clustered regions of secretase activity. These results once validated would be valuable in the field of Alzheimer's Disease research, yet further validation of the approach is required, as the current evidence provided is inadequate to support the conclusions.

Reviewer #1 (Public Review):

Summary:

In their paper, Hou and co-workers explored the use of a FRET sensor for endogenous g-sec activity in vivo in the mouse brain. They used AAV to deliver the sensor to the brain for neuron specific expression and applied NIR in cranial windows to assess FRET activity; optimizing as well an imaging and segmentation protocol. In brief they observe clustered g-sec activity in neighboring cells arguing for a cell non-autonomous regulation of endogenous g-sec activity in vivo.

Strengths:

Mone.

Weaknesses:

Overall the authors provide a very limited data set and in fact only a proof of concept that their sensor can be applied in vivo. This is not really a research paper, but a technical note. With respect to their observation of clustered activity, they now provide an overview image, next to zoomed details. However, from these images one cannot conclude 'by eye' any clustering event. This aligns with the very low r values. All neurons in the field show variable activity and a clustering is not really evident from these examples. Even within a cluster, there is variability. The authors now confirm that expression levels are indeed variable but are independent from the ratio measurements. Further, they controlled for specificity by including DAPT treatments, but opposite to their own in vitro data (in primary neurons) the ratios increased. The authors argue that both distance and orientation can either decrease or increase ratios and that the use of this biosensor should be explored model-by-model. This doesn't really confer high confidence and may hinder other groups in using this sensor reliably.

Secondly, there is still no physiological relevance for this observation. The experiments are performed in wild-type mice, but it would be more relevant to compare this with a fadPSEN1 KI or a PSEN1cKO model to investigate the contribution of a gain of toxic function or LOF to the claimed cell non-autonomous activations. The authors acknowledge this shortcoming but argue that this is for a follow-up study.

For instance, they only monitor activity in cell bodies, and miss all info on g-sec activity in neurites and synapses: what is the relevance of the cell body associated g-sec and can it be used as a proxy for neuronal g-sec activity? If cells 'communicate' g-sec activities, I would expect to see hot spots of activity at synapses between neurons.

Without some more validation and physiologically relevant studies, it remains a single observation and rather a technical note paper, instead of a true research paper.

Reviewer #2 (Public Review):

Summary:

The manuscript by Hou et al is a short technical report which details the potential use of a recently developed FRET based biosensor for gamma-secretase activity (Houser et al 2020) for in vivo imaging in the mouse brain. Gamma-secretase plays a crucial role in Alzheimer's disease pathology and therefore developing methodologies for precise in vivo measurements would be highly valuable to better understand AD pathophysiology in animal models.

The current version of the sensor utilizes a pair of far-red fluorescent proteins fused to a substrate of the enzyme. Using live imaging, it was previously demonstrated it is possible to monitor gamma-secretase activity in cultured cells. Notably, this is a variant of a biosensor that was previously described using CFP-YFP variants FRET pair (Maesako et al, iScience. 2020). The main claim and hypothesis for the manuscript is that IR excitation and emission has considerable advantages in terms of depth of penetration, as well as reduction in autofluorescence. These properties would make this approach potentially suitable to monitor cellular level dynamics of Gama-secretase in vivo.

The authors use confocal microscopy and show it is possible to detect fluorescence from single cortical cells. The paper described in detail technical information regarding imaging and analysis. The data presented details analysis of FRET ratio (FR) measurements within populations of cells. The authors claim it is possible to obtain reliable measurements at the level of individual cells. They compare the FR values across cells and mice and find a spatial correlation among neighboring cells. This is compared with data obtained after inhibition of endogenous gamma-secretase activity, which abolishes this correlation.

Strengths:

The authors describe in detail their experimental design and analysis for in vivo imaging of the reporter. The idea of using a far-red FRET sensor for in vivo imaging is novel and potentially useful to circumvent many of the pitfalls associated with intensity-based FRET imaging in complex biological environments (such as autofluorescence and scattering).

Weaknesses:

There are several critical points regarding the validation of this approach:

(1) Regarding the variability and spatial correlation- the dynamic range of the sensor previously reported in vitro is in the range of 20-30% change (Houser et al 2020) whereas the range of FR detected in vivo is between cells is significantly larger in this MS. This raises considerable doubts for specific detection of cellular activity<br /> (2) One direct way to test the dynamic range of the sensor in vivo, is to increase or decrease endogenous gamma-secretase activity and to ensure this experimental design allows to accurately monitor gamma-secretase activity. In the previous characterization of the reporter (Hauser et al 2020), DAPT application and inhibition of gamma-secretase activity results in increased FR (Figures 2 and 3 of Houser et al). This is in agreement with the design of the biosensor, since FR should be inversely correlated with enzymatic activity. Here, the authors repeated the experiment, and surprisingly found an opposite effect, in which DAPT significantly reduced FR.<br /> The authors maintain that this result could be due to differences in cell-types, However, this experiment was previously performed in cultures cortical neurons and many different cell types, as noted by the authors in their rebuttal.<br /> Instead, I would argue that these results further highlight the concerns of using FR in vivo, since based on their own data, there is no way to interpret this quantification. If DAPT reduces FR, does this mean we should now interpret the results of higher FR corresponds to higher g-sec activity? Given a number of papers from the authors claiming otherwise, I do not understand how one can interpret the results as indicating a cell-specific effect.<br /> In conclusion, without any ground truth, it is impossible to assess and interpret what FR measurements of this sensor in vivo mean. Therefore, the use of this approach as a way to study g-sec activity in vivo seems premature.

Reviewer #3 (Public Review):

This paper builds on the authors' original development of a near infrared (NIR) FRET sensor by reporting in vivo real-time measurements for gamma-secretase activity in the mouse cortex. The in vivo application of the sensor using state-of-the-art techniques is supported by a clear description and straightforward data, and the project represents significant progress because so few biosensors work in vivo. Notably, the NIR biosensor is detectable to ~ 100 µm depth in the cortex. A minor limitation is that this sensor has a relatively modest ΔF as reported in Houser et al, which is an additional challenge for its use in vivo. Thus, the data is fully dependent on post-capture processing and computational analyses. This can unintentionally introduce biases but is not an insurmountable issue with the proper controls that the authors have performed here.

The following opportunity for improving the system didn't initially present itself until the authors performed an important test of the FRET sensor in vivo following DAPT treatment. The authors get credit for diligently reporting the unexpected decrease in 720/670 FRET ratio. In turn this has led to a suggestion that this sensor would benefit from a control that is insensitive to gamma-secretase activity. FRET influences that are independent of gamma-secretase activity could be distinguished by this control.

From previous results in cultured neurons, the authors expected an increase in FRET following DAPT treatment in vivo. These expectations fit with the sensor's mode-of-action because a block of gamma-secretase activity should retain the fluorophores in proximity. When the authors observed decreased FRET, the conclusion was that the sensor performs differently in different cellular contexts. However, a major concern is that mechanistically it is unclear how this could occur with this type of sensor. The relative orientation of fluorophores indeed can contribute to FRET efficiency in tension-based sensors. However, the proteolysis expected with gamma-secretase activity would release tension and orientation constraints. Thus, the major contributing FRET factor is expected to be distance, not orientation. Alternative possibilities that could inadvertently affect readouts include an additional DAPT target in vivo sequestering the inhibitor, secondary pH effects on FRET, photo-bleaching, or an unidentified fluorophore quencher in vivo stimulated by DAPT. Ultimately this new FRET sensor would benefit from a control that is insensitive to gamma-secretase activity. FRET influences that are independent of gamma-secretase activity could be distinguished by this control.

Author response:

The following is the authors’ response to the previous reviews.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

My main concern is still in place. It is unclear whether the proposed method can find actual goal states, and as a result it is unclear what states it finds. Table S1 mentions the model BIOMD0000000454, which is a small metabolic pathway with known equations given in "Example One" in "Metabolic Control Analysis: Rereading Reder". In this model the goal states can be calculated analytically.

Regarding your statements below: I am not concerned that your method will be less efficient than random search (or any other search..) on small models, but I think it is important for the readers to have evidence that your method is able to discover true goal states at least in small networks, used in your study. You do show that your method scales to complex models. So, in my opinion, the missing part is to show that it is able to find true goal states.

"...For simple models whose true steady-state distribution can be derived numerically and/or analytically, it is very likely that their exploration will be much simpler and this is not where a lot of improvement over random search may be found, which explains our focus on more complex models..."

We thank you for your response and for your concerns on the lack of evidence that our method is able to re-discover the true goal states of simple models when these are known a priori. We acknowledge that adding these simple cases is useful for completeness. We did not include these simple models in our main study because in most cases a basic random search over the initial conditions will lead to the re-discovery of these goal states. For instance for the mentioned model BIOMD0000000454 described in the "Example One" from the "Metabolic Control Analysis: Rereading Reder" paper, several simplifying assumptions are made such that the system only has one steady state (x1=0.056, x2=0.769, x3=4.231) which can be found analytically as shown in the paper. In that simple case, this goal state is also straightforward to find with numerical simulation as any valid initial condition will converge to it.

To address the concerns of the reviewer, we propose to add an additional "sanity check" figure in the supplementary of the revised paper (Figure S4), as well as a “sanity check” subsection in the “Methods”, to present additional experiments made on  simple models such as this one. The novel figure and subsection can be visualized on the paper’s interactive version available online https://developmentalsystems.org/curious-exploration-of-grn-competencies, and we plan to include them as such in the further revision.  We have also included the full code to reproduce this sanity check as a ‘sanity_check.ipynb’  jupyter notebook in the github repository (https://github.com/flowersteam/curious-exploration-of-grn-competencies/blob/main/notebooks/sanity_check.ipynb).

In the novel figure S4-b, we show the results of our exploration pipeline on the suggested model BIOMD0000000454 as described in the "Example One" of the paper. These results provide evidence that the curiosity search is able to find back the correct unique goal state (x1=0.056, x2=0.769, x3=4.231), as expected.

We also include a second sanity check on BIOMD0000000341 which models the dynamics of beta-cell mass, insulin and glucose dynamics. This model has two stable fixed points representing physiological (B=300, I=10, G=100) and pathological (B=0, I=0, G=600) steady states, which are the known ground truth steady states as described in Figure 3 of the "A Model of b-Cell Mass, Insulin, and Glucose Kinetics: Pathways to Diabetes" paper. Again, as expected, curiosity search is able to find back those two steady states (Figure S4-a).

As stated in our previous answer, our main study focuses on more complex models that are not limited to one or few attractors that can easily be discovered with random initial conditions. Regarding the mentioned BIOMD0000000454, maybe something that has been confusing for the reviewer is that we indeed included it in our main study but, as specified in the caption of table S4, at the difference of what is done in the "example one" of the original paper, we let the metabolite concentrations y1,...,y5 evolve in time (instead of enforcing them as constants). When doing so, the resulting dynamics of the system are more complex and exhibit a spectrum of possible steady states (unknown a priori), which differ from the previous case with a single steady state. In that case, the new attractors are not analytically easy to find and the proposed curiosity search becomes interesting as it is able to uncover the distribution of possible steady states much more efficiently than a random search baseline, as shown in the new figures S4-c and S4-d.

We hope that these new results will address the reviewer’s concerns and provide evidence to the readers on the validity of the approach on simple networks.

eLife assessment

This important study develops a machine learning method to reveal hidden unknown functions and behavior in gene regulatory networks by searching parameter space in an efficient way. The evidence for some parts of the paper is still incomplete and needs systematic comparison to other methods and to the ground truth, but the work will be of broad interest to anyone working in biology of all stripes since the ideas reach beyond gene regulatory networks to revealing hidden functions in any complex system with many interacting parts.

We thank the editors and reviewers for their positive assessment and constructive suggestions. In our response, we acknowledge the importance of systematic comparison to other methods and to the ground truth, when available. However we also emphasize the challenges associated with evaluating such methods in the context of uncovering hidden behaviors in complex biological networks as the ground truth is often unknown. We hope that our explanations will clarify the potential of our approach in advancing the exploration of these systems.

Public Reviews:

Reviewer #1 (Public Review):

Summary: This paper suggests to apply intrinsically-motivated exploration for the discovery of robust goal states in gene regulatory networks.

Strengths:

The paper is well written. The biological motivation and the need for such methods are formulated extraordinarily well. The battery of experimental models is impressive.

We thank the reviewer for sharing interest in the research problem and for recognizing the strengths of our work.

Weaknesses:

(1) The proposed method is compared to the random search. That says little about the performance with regard to the true steady-state goal sets. The latter could be calculated at least for a few simple ODE (e.g., BIOMD0000000454, `Metabolic Control Analysis: Rereading Reder'). The experiment with 'oscillator circuits' may not be directly interpolated to the other models.

The lack of comparison to the ground truth goal set (attractors of ODE) from arbitrary initial conditions makes it hard to evaluate the true performance/contribution of the method. A part of the used models can be analyzed numerically using JAX, while there are models that can be analyzed analytically.

"...The true versatility of the GRN is unknown and can only be inferred through empirical exploration and proxy metrics....": one could perform a sensitivity analysis of the ODEs, identifying stable equilibria. That could provide a proxy for the ground truth 'versatility'.

We agree with the reviewer that one primary concern is to properly evaluate the effectiveness of the proposed method. However, as we move toward complex pathways, knowledge of the “true” steady-state goal sets is often unknown which is where the use of machine learning methods as the one we propose are particularly interesting (but challenging to evaluate).

For simple models whose true steady-state distribution can be derived numerically and/or analytically, it is very likely that their exploration will be much simpler and this is not where a lot of improvement over random search may be found, which explains our focus on more complex models. While we agree that it is still interesting to evaluate exploration methods on these simple models for checking their behavior, it is not clear how to scale this analysis to the targeted more complex systems.

For systems whose true steady state distribution cannot be derived analytically or numerically, we believe that random search is a pertinent baseline as it is commonly used in the literature to discover the attractors/trajectories of a biological network. For instance, Venkatachalapathy et al. [1] initialize stochastic simulations at multiple randomly sampled starting conditions (which is called a kinetic Monte Carlo-based method) to capture the steady states of a biological system. Similarly, Donzé et al. [29] use a Monte Carlo approach to compute the reachable set of a biological network «when the number of parameters  is large and their uncertain range  is not negligible». For the considered models, the true steady-state goal set is unknown, which is why we chose comparison with random search. We added a “Statistics” subsection in the Methods section providing additional details about the statistical analyses we perform between our method and the random search baseline.

(2) The proposed method is based on `Intrinsically Motivated Goal Exploration Processes with Automatic Curriculum Learning', which assumes state action trajectories [s_{t_0:t}, a_{t_0:t}], (2.1 Notations and Assumptions' in the IMGEP paper). However, the models used in the current work do not include external control actions, but rather only the initial conditions can be set. It is not clear from the methods whether IMGEP was adapted to this setting, and how the exploration policy was designed w/o actual time-dependent actions. What does "...generates candidate intervention parameters to achieve the current goal....", mean considering that interventions 'Sets the initial state...' as explained in Table 2?

We thank the reviewer for asking for clarification, as indeed the IMGEP methodology originates from developmental robotics scenarios which generally focus on the problem of robotic sequential decision-making, therefore assuming state action trajectories as presented in Forestier et al. [65]. However, in both cases, note that the IMGEP is responsible for sampling parameters which then govern the exploration of the dynamical system. In Forestier et al. [65], the IMGEP also only sets one vector at the start (denoted ) which was specifying parameters of a movement (like the initial state of the GRN), which was then actually produced with dynamic motion primitives which are dynamical system equations similar to GRN ODEs, so the two systems are mathematically equivalent. More generally, while in our case the “intervention” of the IMGEP (denoted ) only controls the initial state of the GRN, future work could consider more advanced sequential interventions simply by setting parameters of an action policy  at the start which could be called during the GRN’s trajectory to sample control actions  where  would be the state of the GRN. In practice this would also require setting only one vector at the start, so it would remain the same exploration algorithm and only the space of parameters would change, which illustrates the generality of the approach.

(3) Fig 2 shows the phase space for (ERK, RKIPP_RP) without mentioning the typical full scale of ERK, RKIPP_RP. It is unclear whether the path from (0, 0) to (~0.575, ~3.75) at t=1000 is significant on the typical scale of this phase space. is it significant on the typical scale of this phase space?

The purpose of Figure 2 is to illustrate an example of GRN trajectory in transcriptional space, and to illustrate what “interventions” and “perturbations” can be in that context. To that end we have used the fixed initial conditions provided in the BIOMD0000000647, replicating Figure 5 of Cho et al. [56].

While we are not sure of what the reviewer means with “typical” scale of this phase space, we would like to point reviewer toward Figure 8 which shows examples of certain paths that indeed reach further point in the same phase space (up to ~10 in RKIPP_RP levels and ~300 in ERK levels). However, while the paths displayed in Figure 8 are possible (and were discovered with the IMGEP), note that they may be “rarer” to occur naturally  in the sense that a large portion of the tested initial conditions with random search tend to converge toward smaller (ERK, RKIPP_RP) steady-state values similar to the ones displayed in Figure 2.

(4) Table 2:

a. Where is 'effective intervention' used in the method?

b. in my opinion 'controllability', 'trainability', and 'versatility' are different terms. If their correspondence is important I would suggest to extend/enhance the column "Proposed Isomorphism". otherwise, it may be confusing.

a) We thank the reviewer for pointing out that “effective intervention” is not explicitly used in the method. The idea here is that as we are exploring a complex dynamical system (here the GRN), some of the sampled interventions will be particularly effective at revealing novel unseen outcomes whereas others will fail to produce a qualitative change to the distribution of discovered outcomes. What we show in this paper, for instance in Figure 3a and Figure 4, is that the IMGEP method is particularly sample-efficient in finding those “effective interventions”, at least more than a random exploration. However we agree that the term “effective intervention” is ambiguous (does not say effective in what) and we have replaced it with “salient intervention” in the revised version.

b) We thank the reviewer for highlighting some confusing terms in our chosen vocabulary, and we have clarified those terms in the revised version. We agree that controllability/trainability and versatility are not exactly equivalent concepts, as controllability/trainability typically refers to the amount to which a system is externally controllable/trainable whereas versatility typically refers to the inherent adaptability or diversity of behaviors that a system can exhibit in response to inputs or conditions. However, they are both measuring the extent of states that can be reached by the system under a distribution of stimuli/conditions, whether natural conditions or engineered ones, which is why we believe that their correspondence is relevant.

I don't see how this table generalizes "concepts from dynamical complex systems and behavioral sciences under a common navigation task perspective".

We have replaced the verb “generalize” with “investigate” in the revised version.

Reviewer #2 (Public Review):

Summary:

Etcheverry et al. present two computational frameworks for exploring the functional capabilities of gene regulatory networks (GRNs). The first is a framework based on intrinsically-motivated exploration, here used to reveal the set of steady states achievable by a given gene regulatory network as a function of initial conditions. The second is a behaviorist framework, here used to assess the robustness of steady states to dynamical perturbations experienced along typical trajectories to those steady states. In Figs. 1-5, the authors convincingly show how these frameworks can explore and quantify the diversity of behaviors that can be displayed by GRNs. In Figs. 6-9, the authors present applications of their framework to the analysis and control of GRNs, but the support presented for their case studies is often incomplete.

Strengths:

Overall, the paper presents an important development for exploring and understanding GRNs/dynamical systems broadly, with solid evidence supporting the first half of their paper in a narratively clear way.

The behaviorist point of view for robustness is potentially of interest to a broad community, and to my knowledge introduces novel considerations for defining robustness in the GRN context.

We thank the reviewer for recognizing the strengths and novelty of the proposed experimental framework for exploring and understanding GRNs, and complex dynamical systems more generally. We agree that the results presented in the section “Possible Reuses of the Behavioral Catalog and Framework” (Fig 6-9) can be seen as incomplete along certain aspects, which we tried to make as explicit as possible throughout the paper, and why we explicitly state that these are “preliminary experiments”. Despite the discussed limitations, we believe that these experiments are still very useful to illustrate the variety of potential use-cases in which the community could benefit from such computational methods and experimental framework, and build on for future work.

Some specific weaknesses, mostly concerning incomplete analyses in the second half of the paper:

(1) The analysis presented in Fig. 6 is exciting but preliminary. Are there other appropriate methods for constructing energy landscapes from dynamical trajectories in gene regulatory networks? How do the results in this particular case study compare to other GRNs studied in the paper?

We are not aware of other methods than the one proposed by Venkatachalapathy et al. [1] for constructing an energy landscape given an input set of recorded dynamical trajectories, although it might indeed be the case. We want to emphasize that any of such methods would anyway depend on the input set of trajectories, and should therefore benefit from a set that is more representative of the diversity of behaviors that can be achieved by the GRN, which is why we believe the results presented in Figure 6 are interesting. As the IMGEP was able to find a higher diversity of reachable goal states (and corresponding trajectories) for many of the studied GRNs, we believe that similar effects should be observable when constructing the energy landscapes for these GRN models, with the discovery of additional or wider “valleys” of reachable steady states.

Additionally, it is unclear whether the analysis presented in Fig. 6C is appropriate. In particular, if the pseudopotential landscapes are constructed from statistics of visited states along trajectories to the steady state, then the trajectories derived from dynamical perturbations do not only reflect the underlying pseudo-landscape of the GRN. Instead, they also include contributions from the perturbations themselves.

We agree that the landscape displayed Fig. 6C integrates contributions from the perturbations on the GRN’s behavior, and that it can shape the landscape in various ways, for instance affecting the paths that are accessible, the shape/depth of certain valleys, etc. But we believe that qualitatively or quantitatively analyzing the effect of these perturbations  on the landscape is precisely what is interesting here: it might help 1) understand how a system respond to a range of perturbations and to visualize which behaviors are robust to those perturbations, 2) design better strategies for manipulating those systems to produce certain behaviors

(2) In Fig. 7, I'm not sure how much is possible to take away from the results as given here, as they depend sensitively on the cohort of 432 (GRN, Z) pairs used. The comparison against random networks is well-motivated. However, as the authors note, comparison between organismal categories is more difficult due to low sample size; for instance, the "plant" and "slime mold" categories each only have 1 associated GRN. Additionally, the "n/a" category is difficult to interpret.

We acknowledge that this part is speculative as stated in the paper: “the surveyed database is relatively small with respect to the wealth of available models and biological pathways, so we can hardly claim that these results represent the true distribution of competencies across these organism categories”. However, when further data is available, the same methodology can be reused and we believe that the resulting statistical analyses could be very informative to compare organismal (or other) categories.

(3) In Fig. 8, it is unclear whether the behavioral catalog generated is important to the intervention design problem of moving a system from one attractor basin to another. The authors note that evolutionary searches or SGD could also be used to solve the problem. Is the analysis somehow enabled by the behavioral catalog in a way that is complementary to those methods? If not, comparison against those methods (or others e.g. optimal control) would strengthen the paper.

We thank the reviewer for asking to clarify this point, which might not be clearly explained in the paper. Here the behavioral catalog is indeed used in a complementary way to the optimization method, by identifying a representative set of reachable attractors which are then used to define the optimization problem. For instance here, thanks to the catalog, we 1) were able to identify a “disease” region and several possible reachable states in that region and 2) use several of these states as starting points of our optimization problem, where we want to find a single intervention that can successfully and robustly reset all those points, as illustrated in Figure 8. Please note that given this problem formulation, a simple random search was used as an optimization strategy. When we mention more advanced techniques such as EA or SGD, it is to say that they might be more efficient optimizers than random search. However, we agree that in many cases optimizing directly will not work if starting from random or bad initial guess, and this even with EA or SGD. In that case the discovered behavioral catalog can be useful to better initialize  this local search and make it more efficient/useful, akin to what is done in Figure 9.

(4) The analysis presented in Fig. 9 also is preliminary. The authors note that there exist many algorithms for choosing/identifying the parameter values of a dynamical system that give rise to a desired time-series. It would be a stronger result to compare their approach to more sophisticated methods, as opposed to random search and SGD. Other options from the recent literature include Bayesian techniques, sparse nonlinear regression techniques (e.g. SINDy), and evolutionary searches. The authors note that some methods require fine-tuning in order to be successful, but even so, it would be good to know the degree of fine-tuning which is necessary compared to their method.

We agree that the analysis presented in Figure 9 is preliminary, and thank the reviewer for the suggestion. We would first like to refer to other papers from the ML literature that have more thoroughly analyzed this issue, such as Colas et al. [74] and Pugh et al. [34], and shown the interest of diversity-driven strategies as promising alternatives.  Additionally, as suggested by the reviewer, we added an additional comparison to the CMA-ES algorithm in the revised version in order to complete our analysis. CMA-ES is an evolutionary algorithm which is self-adaptive in the optimization steps and that is known to be better suited than SGD to escape local minimas when the number of parameters is not too high (here we only have 15 parameters). However, our results showed that while CMA-ES explores more the solution space at the beginning of optimization than SGD does, it also ultimately converges into a local minima similarly to SGD. The best solution converges toward a constant signal (of the target b) but fails to maintain the target oscillations, similar to the solutions discovered by gradient descent. We tried this for a few hyperparameters (init mean and std) but always found similar results.  We have updated the figure 9 image and caption, as well as descriptive text, to include these novel results in the revised version. We also added a reference to the CMA-ES paper in the citations.

Reviewer #1 (Recommendations For The Authors):

I would suggest to conduct a more rigor analysis of the performance by estimating/approximating the ground truth robust goal sets in important GRNs.

Also, the use of terminology from different disciplines can be improved. Please see my comments above. Specifically, the connection between controllability in dynamical control systems and versatility used in this paper is unclear.

We hope to have addressed the reviewer's concerns in our previous answers.

Reviewer #2 (Recommendations For The Authors):

Fig 4b: I'm not sure if DBSCAN is the appropriate method to use here, as the visual focus on the core elements of the clusters downplays the full convex hull of the points that random sampling achieves in Z space. An analysis based on convex hulls or the ball-coverage from Fig. 3b would presumably generate plots that were more similar between random sampling and curiosity search. If the goal is to highlight redundancy/non-linearity in the mapping between Z and I, another approach might be to simply bin Z-space in a grid, or to use a clustering algorithm that is less stringent about core/noise distinctions.

We thank the reviewer for the suggestion. This plot is intended to convey the reader an understanding of why a method that uniformly samples goals in Z (what the  IMGEP is doing), is more efficient than a method that uniformly samples parameters in I (what the random search is doing), in systems for which there is high redundancy/non-linearity in the mapping between I and Z. We agree that binning the Z-space in a grid and counting the number of achieved bins is a way to quantitatively measure this, which is by the way very close to what we do in Figure 3 for measuring the achieved diversity. We believe however that the clustering and coloring provides additional intuitions on why this is the case: it illustrates that large regions of the intervention space map to small regions in the outcome space and vice versa.

Additional changes in the revised version:

We added a sentence in the Methods section as well as in the caption of Table S1 providing additional details about the way we simulate the biological models from the BioModels website

We fixed a wrong reference to Figure 4 in the Methods “Sensitivity measure” subsection with reference to Figure 5.

eLife assessment

This important study develops a machine learning method to reveal hidden unknown functions and behaviors in gene regulatory networks by searching parameter space in an efficient way. Solid evidence is presented for the method, which should be of broad interest to anyone working in biology, as the ideas put forward by the authors extend beyond gene regulatory networks to reveal hidden functions in any complex system with many interacting parts.

Reviewer #1 (Public Review):

Summary:

This paper suggests to apply intrinsically-motivated exploration for the discovery of robust goal states in gene regulatory networks.

Strengths:

The paper is well written. The biological motivation and the need for such methods are formulated extraordinarily well. The battery of experimental models is impressive.

Weaknesses:

(1) The proposed method is compared to the random search. That says little about the performance with regard to the true steady-state goal sets. The latter could be calculated at least for a few simple ODE (e.g., BIOMD0000000454, `Metabolic Control Analysis: Rereading Reder'). The experiment with 'oscillator circuits' may not be directly interpolated to the other models.

The lack of comparison to the ground truth goal set (attractors of ODE) from arbitrary initial conditions makes it hard to evaluate the true performance/contribution of the method. A part of the used models can be analyzed numerically using JAX, while there are models that can be analyzed analytically.

"...The true versatility of the GRN is unknown and can only be inferred through empirical exploration and proxy metrics....": one could perform a sensitivity analysis of the ODEs, identifying stable equilibria. That could provide a proxy for the ground truth 'versatility'.

(2) The proposed method is based on `Intrinsically Motivated Goal Exploration Processes with Automatic Curriculum Learning', which assumes state action trajectories [s_{t_0:t}, a_{t_0:t}], (2.1 Notations and Assumptions' in the IMGEP paper). However, the models used in the current work do not include external control actions, but rather only the initial conditions can be set. It is not clear from the methods whether IMGEP was adapted to this setting, and how the exploration policy was designed w/o actual time-dependent actions. What does "...generates candidate intervention parameters to achieve the current goal...."<br /> mean considering that interventions 'Sets the initial state...' as explained in Table 2?

(3) Fig 2 shows the phase space for (ERK, RKIPP_RP) without mentioning the typical full scale of ERK, RKIPP_RP. It is unclear whether the path from (0, 0) to (~0.575, ~3.75) at t=1000 is significant on the typical scale of this phase space. is it significant on the typical scale of this phase space?

(4) Table 2:<br /> (a) Where is 'effective intervention' used in the method?<br /> (b) In my opinion 'controllability', 'trainability', and 'versatility' are different terms. If there correspondence is important I would suggest to extend/enhance the column "Proposed Isomorphism". otherwise, it may be confusing. I don't see how this table generalizes generalizes "concepts from dynamical complex systems and behavioral sciences under a common navigation task perspective".

Reviewer #2 (Public Review):

Summary:

Etcheverry et al. present two computational frameworks for exploring the functional capabilities of gene regulatory networks (GRNs). The first is a framework based on intrinsically motivated exploration, here used to reveal the set of steady states achievable by a given gene regulatory network as a function of initial conditions. The second is a behaviorist framework, here used to assess the robustness of steady states to dynamical perturbations experienced along typical trajectories to those steady states. In Figs. 1-5, the authors convincingly show how these frameworks can explore and quantify the diversity of behaviors that can be displayed by GRNs. In Figs. 6-9, the authors present applications of their framework to the analysis and control of GRNs, but the support presented for their case studies is often incomplete.

Following revision, my overall perspective of the paper remains unchanged. The first half of the paper provides solid evidence to support an important conceptual framework. The evidence presented for the use cases in the latter half is incomplete; as the authors note, they are preliminary and meant to be built on in future work. I have included my first round comments below.

Strengths:

Overall, the paper presents an important development for exploring and understanding GRNs/dynamical systems broadly, with solid evidence supporting the first half of their paper in a narratively clear way.

The behaviorist point of view for robustness is potentially of interest to a broad community, and to my knowledge introduces novel considerations for defining robustness in the GRN context.

Some specific weaknesses, mostly concerning incomplete analyses in the second half of the paper:

(1) The analysis presented in Fig. 6 is exciting but preliminary. Are there other appropriate methods for constructing energy landscapes from dynamical trajectories in gene regulatory networks? How do the results in this particular case study compare to other GRNs studied in the paper?

Additionally, it is unclear whether the analysis presented in Fig. 6C is appropriate. In particular, if the pseudopotential landscapes are constructed from statistics of visited states along trajectories to the steady state, then the trajectories derived from dynamical perturbations do not only reflect the underlying pseudo-landscape of the GRN. Instead, they also include contributions from the perturbations themselves.

(2) In Fig. 7, I'm not sure how much is possible to take away from the results as given here, as they depend sensitively on the cohort of 432 (GRN, Z) pairs used. The comparison against random networks is well-motivated. However, as the authors note, comparison between organismal categories is more difficult due to low sample size; for instance, the "plant" and "slime mold" categories each only has 1 associated GRN. Additionally, the "n/a" category is difficult to interpret.

(3) In Fig. 8, it is unclear whether the behavioral catalog generated is important to the intervention design problem of moving a system in one attractor basin to another. The authors note that evolutionary searches or SGD could also be used to solve the problem. Is the analysis somehow enabled by the behavioral catalog in a way that is complementary to those methods? If not, comparison against those methods (or others e.g. optimal control) would strengthen the paper.

(4) The analysis presented in Fig. 9 also is preliminary. The authors note that there exist many algorithms for choosing/identifying the parameter values of a dynamical system that give rise to a desired time series. It would be a stronger result to compare their approach to more sophisticated methods, as opposed to random search and SGD. Other options from the recent literature include Bayesian techniques, sparse nonlinear regression techniques (e.g. SINDy), and evolutionary searches. The authors note that some methods require fine-tuning in order to be successful, but even so, it would be good to know the degree of fine-tuning which is necessary compared to their method. [second round: the authors have included a comparison against CMA-ES, an evolutionary algorithm]

Reviewer #1 (Public Review):

Yun et al. examined the molecular and neuronal underpinnings of changes in Drosophila female reproductive behaviors in response to social cues. Specifically, the authors measure the ejaculate-holding period, which is the amount of time females retain male ejaculate after mating (typically 90 min in flies). They find that female fruit flies, Drosophila melanogaster, display shorter holding periods in the presence of a native male or male-associated cues, including 2-Methyltetracosane (2MC) and 7-Tricosene (7-T). They further show that 2MC functions through Or47b olfactory receptor neurons (ORNs) and the Or47b channel, while 7-T functions through ppk23 expressing neurons. Interestingly, their data also indicates that two other olfactory ligands for Or47b (methyl laurate and palmitoleic acid) do not have the same effects on the ejaculate-holding period. By performing a series of behavioral and imaging experiments, the authors reveal that an increase in cAMP activity in pC1 neurons is required for this shortening of the ejaculate-holding period and may be involved in the likelihood of remating. This work lays the foundation for future studies on sexual plasticity in female Drosophila.

The conclusions of this paper are supported by the data and the authors have revised the manuscript in accordance with comments of the reviewers. This revised version also contains the expression pattern of the lines used for modulating individual pC1 subtypes. These data and reagents open interesting avenues for future studies on female receptivity and mate choice.

eLife assessment

This important work unravels how female Drosophila can assess their social context via chemosensory cues and modulate the sperm storage process after copulation accordingly. A compelling set of rigorous experiments uncovers specific pheromones that influence the excitability of the female brain receptivity circuit and their propensity to discard inseminate from a mating. This insight into neuronal mechanisms of sexual behavior plasticity is of general interest to scientists working in the fields of animal behavior, neuroscience, evolution, and sexual selection, as well as insect chemosensation and reproduction.

Reviewer #2 (Public Review):

The work by Yun et al. explores an important question related to post-copulatory sexual selection and sperm competition: Can females actively influence the outcome of insemination by a particular male by modulating storage and ejection of transferred sperm in response to contextual sensory stimuli? The present work is exemplary for how the Drosophila model can give detailed insight in basic mechanism of sexual plasticity, addressing the underlying neuronal circuits on a genetic, molecular and cellular level.

Using the Drosophila model, the authors show that the presence of other males or mated females after mating shortens the ejaculate-holding period (EHP) of a female, i.e. the time she takes until she ejects the mating plug and unstored sperm. Through a series of thorough and systematic experiments involving the manipulation of olfactory and chemogustatory neurons and genes in combination with exposure to defined pheromones, they uncover two pheromones and their sensory cells for this behavior. Exposure to the male specific pheromone 2MC shortens EHP via female Or47b olfactory neurons, and the contact pheromone 7-T, present males and on mated females, does so via ppk23 expressing gustatory foreleg neurons. Both compounds increase cAMP levels in a specific subset of central brain receptivity circuit neurons, the pC1b,c neurons. By employing an optogenetically controlled adenyl cyclase, the authors show that increased cAMP levels in pC1b,c neurons increase their excitability upon male pheromone exposure, decrease female EHP and increase the remating rate. This provides convincing evidence for the role of pC1b,c neurons in integrating information about the social environment and mediating not only virgin, but also mated female post-copulatory mate choice.

Understanding context and state-dependent sexual behavior is of fundamental interest. Mate behavior is highly context-dependent. In animals subjected to sperm competition, the complexities of optimal mate choice have attracted a long history of sophisticated modelling in the framework of game theory. These models are in stark contrast to how little we understand so far about the biological and neurophysiological mechanisms of how females implement post-copulatory or so-called "cryptic" mate choice and bias sperm usage when mating multiple times.

The strength of the paper is decrypting "cryptic" mate choice, i.e. the clear identification of physiological mechanisms and proximal causes for female post-copulatory mate choice. The discovery of peripheral chemosensory nodes and of neurophysiological mechanisms in central circuit nodes will provide a fruitful starting point to fully map the circuits for female receptivity and mate choice during the whole gamut of female life history.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Yun et al. examined the molecular and neuronal underpinnings of changes in Drosophila female reproductive behaviors in response to social cues. Specifically, the authors measure the ejaculate-holding period, which is the amount of time females retain male ejaculate after mating (typically 90 min in flies). They find that female fruit flies, Drosophila melanogaster, display shorter holding periods in the presence of a native male or male-associated cues, including 2-Methyltetracosane (2MC) and 7-Tricosene (7-T). They further show that 2MC functions through Or47b olfactory receptor neurons (ORNs) and the Or47b channel, while 7-T functions through ppk23 expressing neurons. Interestingly, their data also indicates that two other olfactory ligands for Or47b (methyl laurate and palmitoleic acid) do not have the same effects on the ejaculate-holding period. By performing a series of behavioral and imaging experiments, the authors reveal that an increase in cAMP activity in pC1 neurons is required for this shortening of the ejaculate-holding period and may be involved in the likelihood of remating. This work lays the foundation for future studies on sexual plasticity in female Drosophila.

The conclusions of this paper are mostly supported by the data, but aspects of the lines used for individual pC1 subtypes and visual contributions as well as the statistical analysis need to be clarified.

(1) The pC1 subtypes (a - e) are delineated based on their morphology and connectivity. While the morphology of these neurons is distinct, they do share a resemblance that can be difficult to discern depending on the imaging performed. Additionally, genetic lines attempting to label individual neurons can easily be contaminated by low-level expression in off-target neurons in the brain or ventral nerve cord (VNC), which could contribute to behavioral changes following optogenetic manipulations. In Figures 5C - D, the authors generated and used new lines for labeling pC1a and pC1b+c. The line for pC1b+c was imaged as part of another recent study (https://doi.org/10.1073/pnas.2310841121). However, similar additional images of the pC1a line (i.e. 40x magnification and VNC expression) would be helpful in order to validate its specificity.

We have included the high-resolution images of the expression of the pC1a-split-Gal4 driver in the brain and the VNC in the new figures S6A and S6B.

(2) The author's experiments examining olfactory and gustatory contributions to the holding period were well controlled and described. However, the experiments in Figure 1D examining visual contributions were not sufficiently convincing as the line used (w1118) has previously been shown to be visually impaired (Wehner et al., 1969; Kalmus 1948). Using another wild-type line would have improved the authors' claims.

It is evident that w1118 flies are visually impaired and are able to receive a limited amount of visual information in dim red light. Nevertheless, they are able to exhibit MIES phenotypes, which further supports the dispensability of visual information in MIES. In a 2024 study, Doubovetzky et al. (1) found that MIES in ninaB mutant females, which have defects in visual sensation, was not altered. This further corroborates our assertion that vision is likely to be of lesser importance than olfaction in MIES.

(3) When comparisons between more than 2 groups are shown as in Figures 1E, 3D, and 5E, the comparisons being made were not clear. Adding in the results of a nonparametric multiple comparisons test would help for the interpretation of these results.

We have revised figures 1E, 3D, 5E and the accompanying legends as suggested.

Reviewer #2 (Public Review):

The work by Yun et al. explores an important question related to post-copulatory sexual selection and sperm competition: Can females actively influence the outcome of insemination by a particular male by modulating the storage and ejection of transferred sperm in response to contextual sensory stimuli? The present work is exemplary for how the Drosophila model can give detailed insight into the basic mechanism of sexual plasticity, addressing the underlying neuronal circuits on a genetic, molecular, and cellular level.

Using the Drosophila model, the authors show that the presence of other males or mated females after mating shortens the ejaculate-holding period (EHP) of a female, i.e. the time she takes until she ejects the mating plug and unstored sperm. Through a series of thorough and systematic experiments involving the manipulation of olfactory and chemo-gustatory neurons and genes in combination with exposure to defined pheromones, they uncover two pheromones and their sensory cells for this behavior. Exposure to the male-specific pheromone 2MC shortens EHP via female Or47b olfactory neurons, and the contact pheromone 7-T, present in males and on mated females, does so via ppk23 expressing gustatory foreleg neurons. Both compounds increase cAMP levels in a specific subset of central brain receptivity circuit neurons, the pC1b,c neurons. By employing an optogenetically controlled adenyl cyclase, the authors show that increased cAMP levels in pC1b and c neurons increase their excitability upon male pheromone exposure, decrease female EHP, and increase the remating rate. This provides convincing evidence for the role of pC1b,c neurons in integrating information about the social environment and mediating not only virgin but also mated female post-copulatory mate choice.

Understanding context and state-dependent sexual behavior is of fundamental interest. Mate behavior is highly context-dependent. In animals subjected to sperm competition, the complexities of optimal mate choice have attracted a long history of sophisticated modelling in the framework of game theory. These models are in stark contrast to how little we understand so far about the biological and neurophysiological mechanisms of how females implement post-copulatory or so-called "cryptic" mate choice and bias sperm usage when mating multiple times.

The strength of the paper is decrypting "cryptic" mate choice, i.e. the clear identification of physiological mechanisms and proximal causes for female post-copulatory mate choice. The discovery of peripheral chemosensory nodes and neurophysiological mechanisms in central circuit nodes will provide a fruitful starting point to fully map the circuits for female receptivity and mate choice during the whole gamut of female life history.

We appreciate the positive response to our work.

Recommendations for the authors:

Reviewing Editor (Recommendations For The Authors):

While appreciating the quality of the work the reviewers had a few key concerns that would greatly improve the manuscript. These are:

(1) In some cases the specific statistical analyses are not clear. Could the authors please clarify what comparisons were made and the specific tests used?

We have clarified the comparisons made in the multiple comparison analysis and specified the tests used in figures 1E, 3D, 5E.

(2) Could the authors please include data that verify the expression patterns of their new reagent for pC1a, which will be useful for the community?

Figure S6 was revised to include the expression of the pC1a-split-Gal4 gene in the brain (Fig. S6A) and the VNC (Fig. S6B).

(3) A figure summarising their findings in the context of known circuitry will be useful.

A new Figure 7 has been prepared, which provides a summary of our findings.

(4) The SAG data are interesting. Do the authors wish to consider moving it to the main text or removing it if too preliminary?

The supplementary figure 10 and related discussions in the discussion section have been removed.

In the revised version of this manuscript, we present new evidence that the Or47b gene is required for 2MC-induced cAMP elevation in pC1 neurons, but not for 7T-induced one (see Fig. 5F). This observation supports that Or47b is a receptor for 2MC.

The following paragraph was inserted at line 248 to provide a detailed description of the new findings: "To further test the role of Or47b in 2MC detection, we generated Or47b-deficient females with pC1 neurons expressing the CRE-luciferase reporter. Females with one copy of the wild-type Or47b allele, which served as the control group, showed robust CRE-luciferase reporter activity in response to either 2MC or 7-T. In contrast, Or47b-deficient females showed robust CRE-luciferase activity in response to to 7-T, but little activity in response to 2MC. This observation suggests that the odorant receptor Or47b plays an essential role in the selective detection of 2MC (Fig. 5F).”

In addition, the following sentence was inserted at line 308 in the discussion section: “In this study, we provide compelling evidence that 2MC induces cAMP elevation in pC1 neurons and EHP shortening via both the Or47b receptor and Or47b ORNs, suggesting that 2MC functions as an odorant ligand for Or47b.”

Relative CRE-luciferase reporter activity of pC1 neurons in females of the indicated genotypes, incubated with a piece of filter paper perfumed with solvent vehicle control or the indicated pheromones immediately after mating. The CRE-luciferase reporter activity of pC1 neurons of Or47b-deficient females (Or47b2/2 or Or47b3/3) was observed to increase in response to 7-T but not to 2MC. To calculate the relative luciferase activity, the average luminescence unit values of the female incubated with the vehicle are set to 100%. Mann-Whitney Test (n.s. p > 0.05; **p < 0.01; ***p < 0.001; ****p < 0.0001). Gray circles indicate the relative luciferase activity (%) of individual females, and the mean ± SEM of data is presented.

Reviewer #1 (Recommendations For The Authors):

(1) There was a discrepancy between the text and the figures. Based on the asterisks above the data in Figure S5A, the data supports only 150 ng of 7-T shortening the ejaculation holding period. However, the text states that (line 190) "150 or 375 ng of 7-T significantly shortened EHP." It would be helpful if the authors clarified this discrepancy.

The sentence has been revised and now reads as follows: ‘150 ng of 7-T significantly shortened EHP’.

(2) Based on the current organization of the text, it was not clear how 2MC was identified and its concentrations were known to be physiologically relevant. It would be helpful if the authors could expand on this in lines 178 - 179.

The following sentences were inserted into the revised version of the manuscript at line 178: The EHP was therefore measured in females incubated in a small mating chamber containing a piece of filter paper perfumed with male CHCs, including 2-methylhexacosane, 2-methyldocosane, 5-methyltricosane, 7-methyltricosane, 10Z-heneicosene, 9Z-heneicosene, and 2MC at various concentrations (not shown). Among these, 2MC at 750 ng was the only one that significantly reduced EHP (Fig. 3A; Fig. S4). 2MC was mainly found in males, but not in virgin females (30). Notably, it is present in D. melanogaster, D. simulans, D. sechellia, and D. erecta, but not in D. yakuba (30, 60).

(3) The inset pie chart image illustrating MIES in Figure 1A was difficult to interpret. It would be helpful if the authors used a different method for representing this (i.e. a timeline).

Figure 1A was revised as suggested.

(4) In lines 121 - 122, the authors state that the females are exposed to "actively courting naive wild type Canton S males." This was difficult to understand and might be improved by removing "actively courting."

Revised as suggested.

Reviewer #2 (Recommendations For The Authors):

(1) Summary figure

The story is quite comprehensive and contains a lot of detail regarding the interaction of signaling pathways, internal state, and sensory stimuli. I believe a schematic summary figure bringing together all findings could be very helpful and would make it much easier to understand the discussion!

Figure 7 has been prepared, which provides a summary of the findings and an explanation of the current working model.

(2) Figure S10/effect on SAG activation of EHP

At the moment, the quite interesting and relevant result that SAG activation shortens EHP shown in Figure S10 is only referred to in the discussion. Maybe move this to the results and give it a bit more attention? Actually, I believe this is a very exciting finding that could also be the basis for some more interesting speculations about physiological relevance. Since SAG is silenced upon seminal fluid/sex peptide exposure after mating, a mating with failed SAG silencing (i.e. unusually high post-mating SAG activity) could indicate to the female that there was low or failed sex peptide/seminal fluid transfer. In such a case it would be probably advantageous for the female to decrease EHP and quickly remate, as females need the "beneficial" effects of seminal fluid on ovulation and physiology adaptation. SAG could therefore represent another arm of sensing male quality- here not via external pheromones, but internally, via sensing male sex peptide levels.

If this is a bit preliminary and rather suited to start a new study, Figure S10 could also be removed from the current manuscript.

Figure S10 and associated text were removed in the revised version of the manuscript.

(3) PhotoAC experiments in pC1b,c: the authors find that raising cAMP levels in pC1b,c leads to a decrease in EHP. They argue that increased cAMP levels lead to higher excitability of pC1b,c. This implies that the activity of pC1b,c promotes mating plug ejection. I assume the authors have also tried activating pC1b,c directly by optogenetic cation channels? What is the outcome of this? If different from elevating cAMP levels: why so?

We employed CsChrimson, a red light-sensitive channelrhodopsin, to investigate the effect of optogenetic activation of each pC1 subset on EHP. Optogenetic activation of pC1a, pC1d, or pC1e had little effect on EHP; however, optogenetic activation of pC1b, c significantly increased EHP. This observation was puzzling because optogenetic silencing of the same neurons also increased EHP. In this experiment, females expressing CsChrimson were exposed to red light for the entire period of EHP measurement. Therefore, we suspect that prolonged activation of pC1b and pC1c neurons depleted their neurotransmitter pool, resulting in a silencing effect, but this requires further testing.

Author response image 1.

The prolonged optogenetic activation of pC1b, c neurons increases EHP, mimicking silencing of pC1b, c neurons. Females of the indicated genotypes were cultured on food with or without all-trans-retinal (ATR). The ΔEHP is calculated by subtracting the mean of the reference EHP of females cultured in control ATR- food from the EHP of individual females in comparison. The female genotypes are as follows: (A) 71G01-GAL4/UAS-CsChrimson, (B) pC1a-split-Gal4/UAS-CsChrimson, (C) pC1b,c-split-Gal4/UAS-CsChrimson, (D) pC1d-split-Gal4/UAS-CsChrimson, and (E) pC1e-split-Gal4/UAS-CsChrimson. Gray circles indicate the ΔEHP of individual females, and the mean ± SEM of data is presented. Mann-Whitney Test (n.s. p > 0.05; *p <0.05; ****p < 0.0001). Numbers below the horizontal bar represent the mean of the EHP differences between the indicated treatments.

(4) Text edits

In general, the manuscript is very well-written, clear, and easy to follow. I recommend small edits of the text and correction of typos in some places:

l.92: "Drosophila females seem to signal the social sexual context through sperm ejection." This sentence could give the impression that the main function of sperm ejection was to signal to conspecifics. I recommend reformulating to leave it open if ejected sperm is a signal or rather a simple cue. e.g. :"There is evidence that Drosophila females detect the social sexual context through sperm ejected by other females."

Thanks for the good suggestion. It has been revised as suggested. In addition, we have also made additional changes to the text to correct typos.

l.97: "transcriptional factor" > "transcription factor"

Revised as suggested. See lines 77, 98, and 201.

l.101: "There are Dsx positive 14 pC1 neurons in each brain hemisphere of the brain," > "There are 14 Dsx positive pC1 neurons in each brain hemisphere,"

Revised as suggested, it now reads " There are 14 Dsx-positive pC1 neurons in each hemisphere of the brain, ...".

l.160: ", even up to 1440 ng" > ", even when applied at concentrations as high as 1440 ng"

Revised as suggested.

l.168: "females with male oenocytes significantly shortens EHP" >"females with male oenocytes significantly shorten EHP"

Revised as suggested.

l.181: "it was restored when Orco expression is reinstated" >"it was restored when Orco expression was reinstated"

Revised as suggested. See line 186.

l.196: "MIES is almost completely abolished" >"MIES was almost completely abolished"

Revised as suggested. See line 201.

l.202: "a sexually dimorphic transcriptional factor gene" >"the sexually determination transcription factor gene" or "the sex specifically spliced transcription factor gene". The gene itself is not dimorphic!

Revised as suggested, lines 208-210 now read "The same study found that Dh44 receptor neurons involved in EHP regulation also express doublesex (dsx), which encodes sexually dimorphic transcription factors."

l.211: "to silenced" > "to silence"

Revised as suggested. See line 216.

l.229: "females that selectively produce the CRE-Luciferase reporter gene" >"females that selectively express CRE-Luciferase reporter"

Revised as suggested. See line 234.

l.271: "neurons. expedite" > delete dot

Revised as suggested. See line 284.

l.287: "Furthermore, our study has uncovered the conserved neural circuitry that processes male courtship cues and governs mating decisions play an important role in regulating this behavior." > grammar: "our study has uncovered that the conserved neural circuitry that processes male courtship cues and governs mating decisions plays an important role in regulating this behavior." Also: the meaning of "conserved" is not fully clear to me here: conserved in regards to other Drosophila species? Or do the authors mean: general functional similarity with mouse sexual circuitry?

The sentence (lines 299-301) has been revised for clarity to read "In addition, our study has revealed that the neural circuit that processes male courtship cues and controls mating decisions plays an important role in regulating this behavior. This fly circuit has recently been proposed to be homologous to VMHvl in the mouse brain (45, 46).”

l.311: "lipid drolet" > "lipid droplets"

Revised as suggested. See line 325.

l.316 and in several instances in the following, including Figure 5 caption (l.723) : "cAMP activity" > "cAMP levels" or "increased cAMP levels"

Revised as suggested.

l.323: "in hemibrain" > ", as seen in the hemibrain connectome dataset"

Revised as suggested. See line 337.

l.326: "increased cAMP levels causes pC1b,c neurons" > "increased cAMP levels cause pC1b,c neurons"

Revised as suggested. See line 340.

l.329: "removement" > "removal" or "ejection"

Revised as suggested, it now reads "the removal of the mating plug". See line 343.

l. 330: "This observation well aligns" > "The observation aligns well"

Revised as suggested. See line 345.

l. 398: Behavior assays: It would be good to describe how mating plug ejection was identified- by eye? Under the microscope/UV light?

The following sentence has been added to the behavioral assays section at lines 425-426: The sperm ejection scene, in which the female expels a white sac containing sperm and the mating plug through the vulva, has been directly observed by eye in recorded video footage.

l.685, Figure legend 2: "thermal activation" > "thermogenetic activation"

Revised as suggested. See line 430.

Reference:

(1) Doubovetzky, N., Kohlmeier, P., Bal, S., & Billeter, J. C. (2023). Cryptic female choice in response to male pheromones in Drosophila melanogaster. bioRxiv, 2023-12.

eLife assessment

This important study aims to move beyond current experimental approaches in speech production by (1) investigating speech in the context of a fully interactive task and (2) employing advanced methodology to record intracranial brain activity. Together these allow for examination of the unfolding temporal dynamics of brain-behaviour relationships during interactive speech. While this approach makes the findings highly compelling, the data are currently deemed incomplete in that neural recordings were only analysed from the left hemisphere (due to insufficient clinical electrode implantation in the right), neglecting the contribution of the right hemisphere.

Reviewer #1 (Public Review):

Summary:

This paper reports an intracranial SEEG study of speech coordination, where participants synchronize their speech output with a virtual partner that is designed to vary its synchronization behavior. This allows the authors to identify electrodes throughout the left hemisphere of the brain that have activity (both power and phase) that correlates with the degree of synchronization behavior. They find that high-frequency activity in the secondary auditory cortex (superior temporal gyrus) is correlated to synchronization, in contrast to primary auditory regions. Furthermore, activity in the inferior frontal gyrus shows a significant phase-amplitude coupling relationship that is interpreted as compensation for deviation from synchronized behavior with the virtual partner.

Strengths:

(1) The development of a virtual partner model trained for each individual participant, which can dynamically vary its synchronization to the participant's behavior in real-time, is novel and exciting.

(2) Understanding real-time temporal coordination for behaviors like speech is a critical and understudied area.

(3) The use of SEEG provides the spatial and temporal resolution necessary to address the complex dynamics associated with the behavior.

(4) The paper provides some results that suggest a role for regions like IFG and STG in the dynamic temporal coordination of behavior both within an individual speaker and across speakers performing a coordination task.

Weaknesses:

(1) The main weakness of the paper is that the results are presented in a largely descriptive and vague manner. For instance, while the interpretation of predictive coding and error correction is interesting, it is not clear how the experimental design or analyses specifically support such a model, or how they differentiate that model from the alternatives. It's possible that some greater specificity could be achieved by a more detailed examination of this rich dataset, for example by characterizing the specific phase relationships (e.g., positive vs negative lags) in areas that show correlations with synchronization behavior. However, as written, it is difficult to understand what these results tell us about how coordination behavior arises.

(2) In the results section, there's a general lack of quantification. While some of the statistics reported in the figures are helpful, there are also claims that are stated without any statistical test. For example, in the paragraph starting on line 342, it is claimed that there is an inverse relationship between rho-value and frequency band, "possibly due to the reversed desynchronization/synchronization process in low and high frequency bands". Based on Figure 3, the first part of this statement appears to be true qualitatively, but is not quantified, and is therefore impossible to assess in relation to the second part of the claim. Similarly, the next paragraph on line 348 describes optimal clustering, but statistics of the clustering algorithm and silhouette metric are not provided. More importantly, it's not entirely clear what is being clustered - is the point to identify activity patterns that are similar within/across brain regions? Or to interpret the meaning of the specific patterns? If the latter, this is not explained or explored in the paper.

(3) Given the design of the stimuli, it would be useful to know more about how coordination relates to specific speech units. The authors focus on the syllabic level, which is understandable. But as far as the results relate to speech planning (an explicit point in the paper), the claims could be strengthened by determining whether the coordination signal (whether error correction or otherwise) is specifically timed to e.g., the consonant vs the vowel. If the mechanism is a phase reset, does it tend to occur on one part of the syllable?

(4) In the discussion the results are related to a previously-described speech-induced suppression effect. However, it's not clear what the current results have to do with SIS, since the speaker's own voice is present and predictable from the forward model on every trial. Statements such as "Moreover, when the two speech signals come close enough in time, the patient possibly perceives them as its own voice" are highly speculative and apparently not supported by the data.

(5) There are some seemingly arbitrary decisions made in the design and analysis that, while likely justified, need to be explained. For example, how were the cutoffs for moderate coupling vs phase-shifted coupling (k ~0.09) determined? This is noted as "rather weak" (line 212), but it's not clear where this comes from. Similarly, the ROI-based analyses are only done on regions "recorded in at least 7 patients" - how was this number chosen? How many electrodes total does this correspond to? Is there heterogeneity within each ROI?

Reviewer #2 (Public Review):

Summary:

This paper investigates the neural underpinnings of an interactive speech task requiring verbal coordination with another speaker. To achieve this, the authors recorded intracranial brain activity from the left hemisphere in a group of drug-resistant epilepsy patients while they synchronised their speech with a 'virtual partner'. Crucially, the authors were able to manipulate the degree of success of this synchronisation by programming the virtual partner to either actively synchronise or desynchronise their speech with the participant, or else to not vary its speech in response to the participant (making the synchronisation task purely one-way). Using such a paradigm, the authors identified different brain regions that were either more sensitive to the speech of the virtual partner (primary auditory cortex), or more sensitive to the degree of verbal coordination (i.e. synchronisation success) with the virtual partner (secondary auditory cortex and IFG). Such sensitivity was measured by (1) calculating the correlation between the index of verbal coordination and mean power within a range of frequency bands across trials, and (2) calculating the phase-amplitude coupling between the behavioural and brain signals within single trials (using the power of high-frequency neural activity only). Overall, the findings help to elucidate some of the left hemisphere brain areas involved in interactive speaking behaviours, particularly highlighting the high-frequency activity of the IFG as a potential candidate supporting verbal coordination.

Strengths:

This study provides the field with a convincing demonstration of how to investigate speaking behaviours in more complex situations that share many features with real-world speaking contexts e.g. simultaneous engagement of speech perception and production processes, the presence of an interlocutor, and the need for inter-speaker coordination. The findings thus go beyond previous work that has typically studied solo speech production in isolation, and represent a significant advance in our understanding of speech as a social and communicative behaviour. It is further an impressive feat to develop a paradigm in which the degree of cooperativity of the synchronisation partner can be so tightly controlled; in this way, this study combines the benefits of using pre-recorded stimuli (namely, the high degree of experimental control) with the benefits of using a live synchronisation partner (allowing the task to be truly two-way interactive, an important criticism of other work using pre-recorded stimuli). A further key strength of the study lies in its employment of stereotactic EEG to measure brain responses with both high temporal and spatial resolution, an ideal method for studying the unfolding relationship between neural processing and this dynamic coordination behaviour.

Weaknesses:

One major limitation of the current study is the lack of coverage of the right hemisphere by the implanted electrodes. Of course, electrode location is solely clinically motivated, and so the authors did not have control over this. However, this means that the current study neglects the potentially important role of the right hemisphere in this task. The right hemisphere has previously been proposed to support feedback control for speech (likely a core process engaged by synchronous speech), as opposed to the left hemisphere which has been argued to underlie feedforward control (Tourville & Guenther, 2011). Indeed, a previous fMRI study of synchronous speech reported the engagement of a network of right hemisphere regions, including STG, IPL, IFG, and the temporal pole (Jasmin et al., 2016). Further, the release from speech-induced suppression during a synchronous speech reported by Jasmin et al. was found in the right temporal pole, which may explain the discrepancy with the current finding of reduced leftward high-frequency activity with increasing verbal coordination (suggesting instead increased speech-induced suppression for successful synchronisation). The findings should therefore be interpreted with the caveat that they are limited to the left hemisphere, and are thus likely missing an important aspect of the neural processing underpinning verbal coordination behaviour.

A further limitation of this study is that its findings are purely correlational in nature; that is, the results tell us how neural activity correlates with behaviour, but not whether it is instrumental in that behaviour. Elucidating the latter would require some form of intervention such as electrode stimulation, to disrupt activity in a brain area and measure the resulting effect on behaviour. Any claims therefore as to the specific role of brain areas in verbal coordination (e.g. the role of the IFG in supporting online coordinative adjustments to achieve synchronisation) are therefore speculative.

eLife assessment

This study presents a valuable finding relating to how the state of arousal is represented within the superior colliculus, a principal visuo-oculomotor structure. The main conclusion that the representation of arousal is segregated, and thus does not directly influence motor output, is incompletely supported by the evidence and the work would be improved if additional analyses were performed to rule out alternative explanations. The work will be of interest to sensory, motor, and cognitive neuroscientists.

Reviewer #1 (Public Review):

Summary:

Johnston and Smith used linear electrode arrays to record from small populations of neurons in the superior colliculus (SC) of monkeys performing a memory-guided saccade (MGS) task. Dimensionality reduction (PCA) was used to reveal low-dimensional subspaces of population activity reflecting the slow drift of neuronal signals during the delay period across a recording session (similar to what they reported for parts of the cortex: Cowley et al., 2020). This SC drift was correlated with a similar slow-drift subspace recorded from the prefrontal cortex, and both slow-drift subspaces tended to be associated with changes in arousal (pupil size). These relationships were driven primarily by neurons in superficial layers of the SC, where saccade sensitivity/selectivity is typically reduced. Accordingly, delay-period modulations of both spiking activity and pupil size were independent of saccade-related activity, which was most prevalent in deeper layers of the SC. The authors suggest that these findings provide evidence of a separation of arousal- and motor-related signals. The analysis techniques expand upon the group's previous work and provide useful insight into the power of large-scale neural recordings paired with dimensionality reduction. This is particularly important with the advent of recording technologies which allow for the measurement of spiking activity across hundreds of neurons simultaneously. Together, these results provide a useful framework for comparing how different populations encode signals related to cognition, arousal, and motor output in potentially different subspaces.

The conclusions drawn by this paper, however, are only partially supported by the data. Additional statistical comparisons and clarifications are needed.

Comments:

(1) The authors make fairly strong claims that "arousal-related fluctuations are isolated from neurons in the deep layers of the SC" (emphasis added). This conclusion is based on comparisons between a "slow drift axis", a low-dimensional representation of neuronal drift, and other measures of arousal (Figures 2C, 3) and motor output sensitivity (Figures 2B, 3B). However, the metrics used to compare the slow-drift axis and motor activity were computed during separate task epochs: the delay period (600-1100 ms) and a peri-saccade epoch (25 ms before and after saccade initiation), respectively. As the authors reference, deep-layer SC neurons are typically active only around the time of a saccade. Therefore, it is not clear if the lack of arousal-related modulations reported for deep-layer SC neurons is because those neurons are truly insensitive to those modulations, or if the modulations were not apparent because they were assessed in an epoch in which the neurons were not active. A potentially more valuable comparison would be to calculate a slow-drift axis aligned to saccade onset.

(2) More generally, arousal-related signals may persist throughout multiple different epochs of the task. It would be worthwhile to determine whether similar "slow-drift" dynamics are observed for baseline, sensory-evoked, and saccade-related activity. Although it may not be possible to examine pupil responses during a saccade, there may be systematic relationships between baseline and evoked responses.

(3) The relationships between changes in SC activity and pupil size are quite small (Figures 2C & 5C). Although the distribution across sessions (Figure 2C) is greater than chance, they are nearly 1/4 of the size compared to the PFC-SC axis comparisons. Likewise, the distribution of r2 values relating pupil size and spiking activity directly (Figure 5) is quite low. We remain skeptical that these drifts are truly due to arousal and cannot be accounted for by other factors. For example, does the relationship persist if accounting for a very simple, monotonic (e.g., linear) drift in pupil size and overall firing rate over the course of an individual session?

(4) It is not clear how the final analysis (Figure 6) contributes to the authors' conclusions. The authors perform PCA on: (i) residual spiking responses during the delay period binned according to pupil size, and (ii) spiking responses in the saccade epoch binned according to target location (i.e., the saccade tuning curve). The corresponding PCs are the spike-pupil axis and the saccade tuning axis, respectively. Unsurprisingly, the spike-pupil axis that captures variance associated with arousal (and removes variance associated with saccade direction) was not correlated with a saccade-tuning axis that captures variance associated with saccade direction and omits arousal. Had these measures been related it would imply a unique association between a neuron's preferred saccade direction and pupil control- which seems unlikely. The separation of these axes thus seems trivial and does not provide evidence of a "mechanism...in the SC to prevent arousal-related signals interfering with the motor output." It remains unknown whether, for example, arousal-related signals may impact trial-by-trial changes in neuronal gain near the time of a saccade, or alter saccade dynamics such as acceleration, precision, and reaction time.

Reviewer #2 (Public Review):

Summary:

Neurons in motor-related areas have increasingly been shown to carry also other, non-motoric signals. This creates a problem of avoidance of interference between the motor and non-motor-related signals. This is a significant problem that likely affects many brain areas. The specific example studied here is interference between saccade-related activity and slow-changing arousal signals in the superior colliculus. The authors identify neuronal activity related to saccades and arousal. Identifying saccade-related activity is straightforward, but arousal-related activity is harder to identify. The authors first identify a potential neuronal correlate of arousal using PCA to identify a component in the population activity corresponding to slow drift over the recording session. Next, they link this component to arousal by showing that the component is present across different brain areas (SC and PFC), and that it is correlated with pupil size, an external marker of arousal. Having identified an arousal-related component in SC, the authors show next that SC neurons with strong motor-related activity are less strongly affected by this arousal component (both SC and PFC). Lastly, they show that SC population activity patterns related to saccades and pupil size form orthogonal subspaces in the SC population.

Strengths:

A great strength of this research is the clear description of the problem, its relationship with the performed analysis, and the interpretation of the results. the paper is very well written and easy to follow.

An additional strength is the use of fairly sophisticated analysis using population activity.

Weaknesses:

(1) The greatest weakness in the present research is the fact that arousal is a functionally less important non-motoric variable. The authors themselves introduce the problem with a discussion of attention, which is without any doubt the most important cognitive process that needs to be functionally isolated from oculomotor processes. Given this introduction, one cannot help but wonder, why the authors did not design an experiment, in which spatial attention and oculomotor control are differentiated. Absent such an experiment, the authors should spend more time explaining the importance of arousal and how it could interfere with oculomotor behavior.

(2) In this context, it is particularly puzzling that one actually would expect effects of arousal on oculomotor behavior. Specifically, saccade reaction time, accuracy, and speed could be influenced by arousal. The authors should include an analysis of such effects. They should also discuss the absence or presence of such effects and how they affect their other results.

(3) The authors use the analysis shown in Figure 6D to argue that across recording sessions the activity components capturing variance in pupil size and saccade tuning are uncorrelated. however, the distribution (green) seems to be non-uniform with a peak at very low and very high correlation specifically. The authors should test if such an interpretation is correct. If yes, where are the low and high correlations respectively? Are there potentially two functional areas in SC?

Reviewer #3 (Public Review):

Summary:

This study looked at slow changes in neuronal activity (on the order of minutes to hours) in the superior colliculus (SC) and prefrontal cortex (PFC) of two monkeys. They found that SC activity shows slow drift in neuronal activity like in the cortex. They then computed a motor index in SC neurons. By definition, this index is low if the neuron has stronger visual responses than motor responses, and it is low if the neuron has weaker visual responses and stronger motor responses. The authors found that the slow drift in neuronal activity was more prevalent in the low motor index SC neurons and less prevalent in the high motor index neurons. In addition, the authors measured pupil diameter and found it to correlate with slow drifts in neuronal activity, but only in the neurons with lower motor index of the SC. They concluded that arousal signals affecting slow drifts in neuronal modulations are brain-wide. They also concluded that these signals are not present in the deepest SC layers, and they interpreted this to mean that this minimizes the impact of arousal on unwanted eye movements.

Strengths:

The paper is clear and well-written.

Showing slow drifts in the SC activity is important to demonstrate that cortical slow drifts could be brain-wide.

Weaknesses:

However, I am concerned about two main points:

First, the authors repeatedly say that the "output" layers of the SC are the ones with the highest motor indices. This might not necessarily be accurate. For example, current thresholds for evoking saccades are lowest in the intermediate layers, and Mohler & Wurtz 1972 suggested that the output of the SC might be in the intermediate layers. Also, even if it were true that the high motor index neurons are the output, they are very few in the authors' data (this is also true in a lot of other labs, where it is less likely to see purely motor neurons in the SC). So, this makes one wonder if the electrode channels were simply too deep and already out of the SC? In other words, it seems important to show distributions of encountered neurons (regardless of the motor index) across depth, in order to better know how to interpret the tails of the distributions in the motor index histogram and in the other panels of Figure Supplement 1. I elaborate more on these points in the detailed comments below.

Second, the authors find that the SC cells with a low motor index are modulated by pupil diameter. However, this could be completely independent of an "arousal signal". These cells have substantial visual responses. If the pupil diameter changes, then their activity should be influenced since the monkey is watching a luminous display. So, in this regard, the fact that they do not see "an arousal signal" in most motor neurons (through the pupil diameter analyses) is not evidence that the arousal signal is filtered out from the motor neurons. It could simply be that these neurons simply do not get affected by the pupil diameter because they do not have visual sensitivity. So, even with the pupil data, it is still a bit tricky for me to interpret that arousal signals are excluded from the "output layers" of the SC.

I think that a remedy to the first point above is to change the text to make it a bit more descriptive and less interpretive. For example, just say that the slow drifts were less evident among the neurons with high motor index.

For the second point, I think that it is important to consider the alternative caveat of different amounts of light entering the system. Changes in light level caused by pupil diameter variations can be quite large.

eLife assessment

Sisigano et al. report findings about the role of sphingolipids using lipidomics with machine learning in paclitaxel-induced peripheral neuropathy and preliminary translation of the impact of SA1P in cultured neuronal cells. This study presents a valuable finding on the increased activity of two well-studied signal transduction pathways in a subtype of breast cancer. The significance is limited by incomplete evidence which can be addressed in larger clinical cohorts in the future and with more robust biological validation approaches.

Reviewer #1 (Public Review):

Summary:

This study examines lipid profiles in cancer patients treated with the neurotoxic chemotherapy paclitaxel. Multiple methods, including machine learning as well as more conventional statistical modelling, were used to classify lipid patterns before and after paclitaxel treatment and in conjunction with neuropathy status. Lipid profiles before and after paclitaxel therapy were analysed from 31 patients. The study aimed to characterize from the lipid profile if plasma samples were collected pre paclitaxel or post paclitaxel and their relevance to neuropathy status. Sphingolipids including sphinganine-1-phosphate (SA1P) differed between patients with and without neuropathy. To examine the potential role of SA1P, it was applied to murine primary sensory neuron cultures, and produced calcium transients in a proportion of neurons. This response was abolished by application of a TRPV1 antagonist. The number of neurons responding to SA1P was partially reduced by the sphingosine 1-phosphate receptor (S1PR1) modulator fingolimod.

Strengths:

The strengths of this study include the use of multiple methods to classify lipid patterns and the attempt to validate findings from the clinical cohort in a preclinical model using primary sensory neurons.

Weaknesses:

These still stand from the original review and are repeated here:

There are a number of weaknesses in the study. The small sample size is a significant limitation of the study. Out of 31 patients, only 17 patients were reported to develop neuropathy, with significant neuropathy (grade 2/3) in only 5 patients. The authors acknowledge this limitation in the results and discussion sections of the manuscript, but it limits the interpretation of the results. Also acknowledged is the limited method used to assess neuropathy.

Potentially due to this small number of patients with neuropathy, the machine learning algorithms could not distinguish between samples with and without neuropathy. Only selected univariate analyses identified differences in lipid profiles potentially related to neuropathy.

Three sphingolipid mediators including SA1P differed between patients with and without neuropathy at the end of treatment. These sphingolipids were elevated at end of treatment in the cohort with neuropathy, relative to those without neuropathy. However, across all samples from pre to pos- paclitaxel treatment, there was a significant reduction in SA1P levels. It is unclear from the data presented what the underlying mechanism for this result would be. If elevated SA1P is associated with neuropathy development, it would be expected to increase in those who develop neuropathy from pre to post-treatment timepoints.

Primary sensory neuron cultures were used to examine the effects of SA1P application. SA1P application produced calcium transients in a small proportion of sensory neurons. It is not clear how this experimental model assists in validating the role of SA1P in neuropathy development as there is no assessment of sensory neuron damage or other hallmarks of peripheral neuropathy. These results demonstrate that some sensory neurons respond to SA1P and that this activity is linked to TRPV1 receptors. However, further studies will be required to determine if this is mechanistically related to neuropathy.

Impact:

Taken in total, the data presented do not provide sufficient evidence to support the contention that SA1P has an important role in paclitaxel induced peripheral neuropathy. Further, the results do not provide evidence to support the use of S1PR1 receptor antagonists as a therapeutic strategy. It is important to be careful with language use in the discussion, as the significance of the present results are overstated.

However, based on the results of previous studies, it is likely that sphingolipid metabolism plays a role in chemotherapy induced peripheral neuropathy. Based on this existing evidence, the S1PR1 receptor antagonist fingolimod has already been examined in experimental models and in clinical trials. Further work is needed to examine the links between lipid mediators and neuropathy development and identify additional strategies for intervention.

eLife assessment

This study presents a valuable finding that pathways associated with ribosome biogenesis (RiBi) are activated during transition cell states and targeting ribosome biogenesis could be a viable approach to overcome EMT-related chemoresistance in BCs. The evidence supporting the claims of the authors is quite solid, although inclusion of additional experimental support that blocking of EMT/MET is necessary for the synergistic effect of standard chemotherapy together with RiBi blockage would have strengthened the study. The work will be of interest to scientists working on breast cancer.

Reviewer #1 (Public Review):

The process of EMT is a major contributor of metastasis and chemoresistance in breast cancer. By using a modified PyMT model that allows identification of cells undergoing EMT and their decedents via S100A4-Cre mediated recombination of the mTmG allele, Ban et al. tackle a very important question of how tumor metastasis and therapy resistance by EMT can be blocked. They identified that pathways associated with ribosome biogenesis (RiBi) are activated during transition cell states. This finding represents a promising therapeutic target to block any transition from E to M (activated during cell dissemination and invasion) as well as from M to E (activated during metastatic colonization). Inhibition of RiBi-blocked EMT also reduced the establishment of chemoresistance that is associated with an EMT phenotype. Hence, RiBi blockage together with standard chemotherapy showed synergistic effects, resulting in impaired colonization/metastatic outgrowth in an animal model. The study is of great interest and of high clinical relevance as the authors show that blocking the transition from E to M or vice versa targets both aspects of metastasis, dissemination form the primary tumor and colonization in distant organs.

The study is done with high skill using state of the art technology and the conclusions are convincing and solid, but some aspects require some additional experimental support and clarification. It remains elusive whether blocking of EMT/MET is necessary for the synergistic effect of standard chemotherapy together with RiBi blockage or whether a general growth disadvantage of RiBi treated cells independent of blocking transition is responsible. How can specific effect on state transition by RiBI block be seperated from global effects attributed to overall reduced protein biosynthesis, proliferation etc.? Some other aspects are misleading or need extension:

In the revised version, the authors appropriately addressed all my comments. I'd like to congratulate the authors for this wonderful work!

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review): 

The process of EMT is a major contributor to metastasis and chemoresistance in breast cancer. By using a modified PyMT model that allows the identification of cells undergoing EMT and their decedents via S100A4-Cre mediated recombination of the mTmG allele, Ban et al. tackle a very important question of how tumor metastasis and therapy resistance by EMT can be blocked. They identified that pathways associated with ribosome biogenesis (RiBi) are activated during transition cell states. This finding represents a promising therapeutic target to block any transition from E to M (activated during cell dissemination and invasion) as well as from M to E (activated during metastatic colonization). Inhibition of RiBi-blocked EMT also reduced the establishment of chemoresistance that is associated with an EMT phenotype. Hence, RiBi blockage together with standard chemotherapy showed synergistic effects, resulting in impaired colonization/metastatic outgrowth in an animal model. The study is of great interest and of high clinical relevance as the authors show that blocking the transition from E to M or vice versa targets both aspects of metastasis, dissemination from the primary tumor, and colonization in distant organs. 

We appreciate the positive acknowledgment of our work.

The study is done with high skill using state-of-the-art technology and the conclusions are convincing and solid, but some aspects require some additional experimental support and clarification. It remains elusive whether blocking of EMT/MET is necessary for the synergistic effect of standard chemotherapy together with RiBi blockage or whether a general growth disadvantage of RiBi-treated cells independent of blocking transition is responsible. 

We appreciate the reviewer for raising the pertinent query regarding the interrelation between EMT/MET blocking by RiBi inhibition and its synergistic effect with chemotherapy drugs. Our experimental data suggests a potential consequence of these events. Specifically, when assessing the potency of RiBi inhibitors (BMH21 and CX5410), we observed a pronounced EMT/MET blocking effect at concentrations preceding the emergence of cytotoxic effects (refer to Fig. 4 and Supplementary Fig S8). Notably, the IC50 for BMH21 was approximately 200nM, which is a concentration surpassing those that manifested the EMT/MET blocking effects. Crucially, the enhanced synergy of RiBi inhibitors with chemotherapy drugs was predominantly seen at these lower concentrations (as illustrated in Supplementary Fig S10). Therefore, the EMT/MET blocking by RiBi inhibition, rather than the cytotoxic effect, is likely instrumental for the synergy with chemotherapy drugs. The result was highlighted in Page#16.

How can specific effects on state transition by RiBI block be separated from global effects attributed to overall reduced protein biosynthesis, proliferation etc.? 

We appreciate the reviewer's insightful query. We agree that RiBi activity and associated protein synthesis are fundamental processes for cell viability, making it challenging to clearly delineate the overall effects of RiBi blockage to the specific effects of EMT state transition. Our results showed an elevated RiBi activity during the EMT transitioning phases, concomitant with enhanced nascent protein synthesis, indicating a higher-than-normal requirement of new proteins for cells to switch their phenotype. This would provide us a chance to target the excessive activities of RiBi to block EMT/MET transition. Based on a similar consideration, we chose to apply shRNA instead of CRISPR technology to modulate RiBi gene expression. By comparing to scramble controls, the growth rates of the Rps knockdown cells (both RFP+ and GFP+ cells) were not significantly affected, while the EMT/MET transitioning was impaired (Supplementary Fig 9). These results may provide evidence of uncoupling the cell proliferation and EMT/MET status changes by inhibiting RiBi pathway.  

Some other aspects are misleading or need extension. 

Reviewer #1 (Recommendations For The Authors): 

(1) The analysis of RiBi expression during EMT in Fig. 1K shows that transition states have high RiBi levels, whereas E and M states are low. Analyses of MET in Fig.2G indicate that M states have the lowest, transition states upregulate RiBi while E states have the highest levels of RiBi expression. This is puzzling and how can it be explained? It would be helpful to demonstrate how these two settings are related by combining results from Figs 1 and 2 in an E-Trans-M-Trans-E state graph (in a sequence of EMT/MET). Does it mean that the initial E state starts with lower RiBi and the final E state displays the highest RiBi expression? In other words, are the initial E state and the one after MET different? 

Thank the reviewer for raising the concern about which EMT/MET state exhibits the highest RiBi activity. Following the reviewer's suggestions, we merged the scRNA-seq data of EMT and MET cells and performed the trajectory analysis. Similar epithelial-mesenchymal spectrums were detected from these cells (For reviewers Fig 1). Notably, the highest RiBi activity was detected in the early EMT transitioning or the late MET transitioning cells (revised For reviewers Fig 1D). Addressing the question of the reviewer, the initial E state (of EMT cells) did not show significant differences to the final E state (of MET cells) in comparisons of EMT pseudotime and RiBi activities. In addition, the analysis with merged cells also revealed:

(1) Both the EMT (In_Vitro_Mix) and MET (In_Vivo_GFP) cells were generally divided into two major clusters representing epithelial and mesenchymal phenotypes (For reviewers Fig 1A, 1B).

(2) The EMT and MET cells exhibited similar EMT spectrums (EMT/MET status, and pseudotime) in the trajectory analysis (For reviewers Fig 1C, 1D).

(3) Cells with high RiBi activity were mostly from the transitioning cell during EMT (In_Vitro_Mix) cells (For reviewers Fig 1D).  

(2) It needs to be elaborated on how the experiment in Fig. 4A was exactly done. Are there cells isolated directly from the autochthonous TriPyMT tumor in contrast to steady-state cultures from Fig. 1? Does the control graph represent 0d in culture or have the cells been cultured for the same amount of time as the treated samples? How do these observed 15% GFP+ cells are related to the 15% GFP+ cells obtained at day 0 and 34% at d7 control condition in Fig. 5A? 

Following the reviewer’s suggestion, we have amended the figure legend to clarify the experiment settings. In Fig. 4A, we initiated the experiment with sorted RFP+/Epcam+ cells. The control cells were cultured for the same period of time (5 days) as drug-treated cells did. We apologize for the unclear description. The percentage of GFP+ cells in this experiment is not related to the experiment in Fig 5A, where the initial cell population comprised an unsorted mix of RFP/GFP cells. 

(3) Fig. 4B: Since the bulk population is loaded in the WB, does that suggest that the epithelial state is stabilized/enhanced or does it reflect only different cell ratios? So, it would be important to show the WB for RFP+ and GFP+ cells separately. 

Thank the reviewer for the query regarding Fig. 4B. We apologize for the unclear explanation. The experimental setup for Fig 4B was identical to that of Fig 4A, where the sorted RFP+ cells were utilized at the start. Indeed, the observed increase in epithelial markers and decrease in mesenchymal markers in cells treated with BMH and CX suggest a higher proportion of cells maintaining the RFP+ state. 

Performing WB for RFP+ and GFP+ cells separately may not address the question we asked since the experiment was initialed with pure RFP+ cells. Also, the expression of the fluorescent markers is closely aligned with the EMT status of the cells with and without drug treatment.  

(4) Figs. 4-6: The authors claim that there is less EMT under treatment. If the experiment was done over 5 days (as indicated in Fig.4b legend), it is necessary to rule out that shifts in E/M ratios are attributed to the effects of treatment on proliferation/survival affecting both populations differently. How do the same cells grow under treatment when injected orthotopically/subcutaneously? 

We apologized for the unclear descriptions. The effect of blocking the transitioning of EMT with RiBi inhibitors were performed with purified RFP+/EpCam+ cells. All GFP+ cells in this experiment setting were transformed from RFP+ cells. Given the fluorescence switch was well correlated with EMT status of cells, RFP and GFP were used as EMT reporters. Similarly, we used purified GFP+/EpCam- cells as the initial population to study the MET process of tumor cells.

To address the reviewer's concern regarding how RiBi inhibition may differentially affect the growth of RFP+ and GFP+ cells, we conducted a cell cycle assay using Tri-PyMT cells, which include both RFP+ and GFP+ populations. Our results demonstrated that both RFP+ and GFP+ cells exhibited a trend towards G2/M phase accumulation when treated with BMH21. It is important to note that the impact of BMH21 on the cell cycle was less pronounced than previously reported by Fu et al. (Oncol Rep, 2017). This is likely because the dose used for EMT inhibition in our study was approximately one-tenth of the dose known to inhibit cell growth (For Reviewers Fig 2). Also, no significantly differential impacts were detected between RFP+ and GFP+ cells. 

We have previously characterized the proliferation rate of RFP+ and GFP+ populations (Lourenco et al 2020). RFP+ cells proliferate faster than GFP+ cells. Primary tumor cells derived from RFP+ cells also grew faster than GFP+ tumors (Lourenco et al 2020).

(5) Fig. 6B: this image is puzzling. Only in the lower two panels the outline of the lung is visualized by DAPI staining. The upper two panels look like there is no lung tissue in ctrl (no DAPI+GFP-RFP- cells) or show almost exclusively DAPI+GFP-RFP- cells that are present in a clustered assembly. Do the latter represent lymphoid cell clusters or normal lung tissue? 

To improve the clarity of fluorescent images in Fig 6B, we enlarged the merge images with higher contrast (Revised Fig. 6B). The DAPI+/RFP-/GFP- region represent normal lung tissue. Nodules with either RFP or GFP signals represent tumor lesions.  

(6) Text: Several typos and sentences should be revised, including p. 3 "Le et al. discovered" which should read as "Li et al. discovered", p.8 "Vimten", p.10 "Cells were then classified cells into three main categories", GSEA should be spelled out as Gene Set Enrichment Analysis (not Assay), p. 13 "cells, suggesting the impaired MET capability with upon treatment". 

We apologize for the typos. All were corrected in the revised manuscript.

(7) Figures: Color gradient indicator in Fig. 1E does not reflect the colors of the cells, Fig. S5A+C are not referenced in the text, there is mislabeling of S5B,C,D in the legend, graph in Fig. 3D is placed two times and overlapping, Fig. 6C labeling needs adjustments, labeling of Fig. 6D should be similar to Fig. 6A: CTX blue and BMH21 green. 

We apologize for these errors and made corrections. Color in Fig.1E represents the EMT status of tumor cells as indicated in the revised figure, red for more epithelial, and green for more mesenchymal features. Fig S5 is now Fig S6, and referred in the revised manuscript. Legend for figures were corrected. Labels of Fig 6 were adjusted. 

Reviewer #2 (Public Review): 

(1) The current manuscript by Ban et al describes that cells undergoing EMT have increased rRNA synthesis, as analyzed by RNA seq-based gene expression analysis, and that the increased rRNA synthesis provides a therapeutic opportunity to target chemoresistance. The cells utilized in this manuscript were isolated from the authors' Tri-PyMT EMT lineage tracing model published a few years ago which demonstrated that cells undergoing EMT are not the cells that are contributing to metastasis but rather to tumor chemoresistance (Fischer, Nature 2015). This in vivo model has since then been criticized for not capturing all relevant EMT events which the authors also acknowledge in the introduction. The authors therefore reason that they use this lineage tracing model to better understand the role of EMT in chemoresistance. 

A major problem with the current manuscript is that the authors present many of their findings as a novel without the proper acknowledgment of previously published literature in particular, Prakash et al., Nature Communications, 2019 and Dermitt, Dev Cell, 2020. In the studies by Prakash, the authors demonstrate that maintaining ongoing rRNA biogenesis is essential for the execution of the EMT program, and thus the ability of cancer cells to become migratory and invasive. Further, Prakash et al showed that blocking rRNA biogenesis with a small molecule inhibitor, CX-5461 (which is also used in the study by Ban et al) specifically inhibits breast cancer growth, invasion, EMT, and metastasis in animal models without significant toxicity to normal tissues. As such a significant revision that is necessary at this time is a rewrite of the manuscript especially the introduction and the discussion to more accurately describe and cite previously published findings and then highlight the current work by Ban et al which nicely builds on the previously published literature as it highlights the contribution of EMT to chemoresistance rather than metastasis. The suggestion for the authors is that they therefore should focus on highlighting the chemotherapy resistance angle as their Tri-PyMT EMT lineage tracing was chosen to test this angle and as such focus on both primary tumor growth and metastasis. 

We appreciate the reviewer’s insightful feedback. In response, we have revised a section in the discussion to better highlight how our study builds upon and extends the work of others. We acknowledge that the link between ribosome biogenesis (RiBi) and the epithelial-mesenchymal transition (EMT) pathway was noted by prior researches (Prakash et al. 2019; Ebright et al. 2020). In the revised manuscript, we have included extra discussion about the topic. Our findings, however, contribute to this knowledge by elucidating increased activities of RiBi during both EMT and mesenchymal-epithelial transition (MET) processes, thereby deepening our understanding of its role. Additionally, we have clarified our novel stance on EMT-targeting strategies. Rather than solely targeting the mesenchymal phenotype, we propose that inhibiting the phenotypic switching ability of tumor cells (a round trip encompassing both EMT and MET) could be more effective, as described in the introduction part.

Additional major revisions: 

(2) The authors use the FSP1-Cre Model which in the field has been questioned as to not capture all the relevant EMT events and therefore their findings should be corroborated by another EMT model system. 

We agree with the reviewer that the Fsp1-Cre model could not capture ALL the relevant EMT events. However, the fidelity and accuracy of Fsp1-Cre model in reporting EMT process of Tri-PyMT cells have also been demonstrated in our previous studies (Lourenco et al. 2020). Also, we have included additional results to further characterize this model: 1) Continuous fluorescence switching from RFP+ to GFP+ was observed in Tri-PyMT cells (Supplementary Fig S1); 2) Bulk RNA-seq data showed the differential expression of EMT marker genes with the RFP+ and GFP+ cells (Supplementary Fig S2A); 3) Single-cell RNA-seq data showed the EMT spectrum and EMT status distributions according to Fsp1(S100a4)/Epcam, and Vim/Krt18 expression (revised Supplementary Fig S3B, 3C). Hope these results clarify the reviewer’s doubt about the Fsp1-Cre model in reporting EMT of tumor cells. Of note, the evaluation of EMT status with RiBi activity does not rely solely on the fluorescent marker switch but on the ETM-related transcriptome (EMTome) of the Tri-PyMT cells. 

Again, we agree with the reviewer that the Tri-PyMT model does not report ALL relevant EMT events. In the manuscript, we have included experiments with MD-MB231-LM2 cells (Fig 6D) and analyzed the sequencing databases of breast cancer patients (revised Supplementary Fig S13, S14), to validate the findings of the association between EMT status and RiBi activity.

(3) In the current version of the manuscript, there are no measurements of rRNA synthesis, but the gene expression profiles are used as a proxy for rRNA synthesis. The authors therefore need to include measurements of rRNA synthesis corroborating the RNA sequencing data to support their scientific findings and claims. This can be accomplished by qPCR, Northern blot, or EU staining of the respective sorted cell population. Quantification of rRNA synthesis is also needed for the CX5461/BMH-21 and silencing studies. 

We agree that direct measure rRNA synthesis is important to validate the association of RiBi activity with the EMT/MET process. Following the reviewer’s suggestion, we performed EU incorporation assay with RFP+, Double+, and GFP+ Tri-PyMT cells with and without RiBi inhibitors. Under the treatment-naïve condition, the double+ (EMT-transitioning) cells exhibited highest activity of rRNA synthesis compared to either RFP+ (E) and GFP+ (M) cells (revised Supplementary Fig S7). Also, as expected, the treatment of BMH21 or CX-5461 could significantly inhibit the rRNA synthesis (revised Supplementary Fig S8B).

(4) Currently, there is no mechanistic insight as to how rRNA synthesis is increased during EMT, which would also strengthen the manuscript. This could be done through targeted ChIP analysis. 

The experimental data in the current manuscript suggest that the activation of RiBi is upstream of the EMT process, as the impaired RiBi pathway hinders the EMT of tumor cells. We are uncertain about the suggestion regarding ChIP analysis. If the reviewer refers to ChIP analysis with EMT transcription factors (i.e., Snail, Twist, and Zeb1), it may not elucidate the mechanisms by which the EMT process is associated with rRNA synthesis. Using sorted GFP/RFP double-positive Tri-PyMT cells, we found enhanced activations in the ERK and mTOR pathways in the EMT-transitioning cells (Figure 3A). It is well-documented that the ERK and mTOR pathways are key coordinators of EMT (Xie et al., Neoplasia 2004; Shin et al., PNAS 2019; Lamouille et al., J. Cell Sci. 2012; Roshan et al., Biochimie 2019). Interestingly, we also observed significantly higher phosphorylation of rpS6, a downstream indicator of mTOR pathway activation, in the Doub+ cells. As an indispensable ribosome protein, rpS6 phosphorylation could impact ribosome functions of protein translation (Bohlen et al., Nucleic Acid Res. 2021; Mieulet et al., 2007).

(5) rRNA synthesis has canonically been linked to the cell cycle therefore it will be necessary for the authors to determine the cell cycle state of their respective cell populations throughout the manuscript. 

Following the reviewer's suggestion, we analyzed the cell cycles of RFP+, GFP+, and Doub+ Tri-PyMT cells. Our analysis revealed that the proportion of proliferating RFP+ cells (in the S phase) was higher than that of proliferating GFP+ cells. Interestingly, the Doub+ cells also exhibited a higher ratio of proliferation, which was significantly greater compared to both RFP+ and GFP+ cells (revised supplementary Figure S1B).

(6) Statistics and quantifications are currently missing in several figures and need to be better explained throughout the manuscript to strengthen the scientific rigor of the studies. 

We have improved the clarity of our manuscript. Proper statistics descriptions of experiments have been carefully reviewed and adequate information was edited in the revised manuscript.

(7) Only metastasis studies are shown in the current version of the manuscript. These studies should be complemented with primary tumor studies as the main focus of the paper is the contribution of EMT to chemoresistance. 

We appreciate the reviewer's suggestion regarding the primary tumor studies. We apologize for not stating clearly in our manuscript. In response, we have revised the manuscript to outline the rationale for establishing a competitive model by injecting a mixture of RFP+ and GFP+ cells in a 1:1 ratio via the tail vein. This model is designed to study of both EMT and MET processes under chemotherapy at a distal site, where tumor cells need phenotypic switches (both EMT and MET) to adapt to and overcome chemo/environmental challenges in this context. Indeed, we have studied the primary tumor growth with the pre-EMT (RFP+) and postEMT (GFP+) cells. Their differential contribution to tumor growth was published in another paper (Lourenco etal. Cancer Res 2020). 

Reviewer #2 (Recommendations For The Authors): 

Figure 1 and associated supplementary figure panels 

Fig. 1A. More details are needed about the Tri-PyMT model and the induction of EMT in vitro. The authors mention that when growing the isolated cells they spontaneously undergo EMT when grown in 10% FBS. What is the timeline for this transition and how reproducible is it? This information is not clear from Supp. 1. When were cells taken for analysis and also how long is plasticity maintained? According to Supp 1. cell generation 15-21 seems to have a stable cell population of green, red, and yellow cells. Are these cell populations changing if one stimulates the whole cell population with a pro-EMT stimulus? Since cell proliferation is linked to rRNA synthesis the authors also need to include markers of cell cycle for the individual cell population to identify which cell cycle state each sorted cell population is associated with. 

We thank the reviewer for recommending further analysis of the cell cycle among RFP+, GFP+, and Doub+ cells. As illustrated in the revised Supplementary Figure 1B, an increased proportion of RFP+ cells was observed in the S phases in comparison to GFP+ cells. Conversely, Doub+ cells demonstrated a proliferation rate even higher than to that of RFP+ cells.

Upon sorting, RFP+ cells were found to spontaneously undergo epithelial-mesenchymal transition (EMT) when cultured in 10% FBS media, thereby converting to GFP+. We quantified the GFP+ cell percentage within the total cell population, noting a consistent transition of a certain proportion of RFP+ cells to EMT, leading to an accumulation of GFP+ cells. This accumulation stabilizes as approximately 60-70% of the entire population become GFP+. Remarkably, re-sorting RFP+ cells from this balanced tumor cell population resulted in a similar fluorescent transition pattern as observed in the parental population. The mechanisms by which tumor cells regulate the EMT phenotypes across the entire population remain unclear. Nevertheless, the equilibrium between RFP+ and GFP+ cells may be attributed in part to the more rapid proliferation of RFP+ cells and the limited proportion of tumor cells undergoing EMT.

We conducted repeated long-term cultures (up to 20 passages) of the Tri-PyMT cells, yielding consistent results. The fluorescence transition pattern in Tri-PyMT cells proved highly reliable. Further details regarding the Tri-PyMT cells have been incorporated into the Methods section.

Fig. 1B. The loading control is not even and quantification is missing, in the text, it states Vimten instead of Vimentin. 

The less loading with Doub+ cells was due to the limited number of EMT transitioning cells we could purify by flow sorting. Even though, the expression of both epithelial and mesenchymal markers in the Doub+ cells were clear. In the revised manuscript, we have quantified the Western blot results. We also apologize for the type errors and have corrected the spelling of "Vimentin."

Fig. 1K. In this figure, the authors write: 'It is worth noting that with the 2-phase classifications (Epi or Mes), the elevated RiBi activity was associated with the transitioning cells still exhibiting overall epithelial phenotypes; RiBi activities diminished as cells completed their transition to the mesenchymal phase'. But in Fig. 1K, the Ribi activity is already at a peak during the epithelial state and starts declining already at the beginning of the transition, can the authors please explain this data a bit more? The finding that ribosome biogenesis diminishes once the cells have completed their transition was shown in Prakash et al, Fig. 1 J, I, and accordingly their scientific findings should be discussed in the context of published work. 

We acknowledge the reviewer's concerns regarding the comparison of the timeline for EMT in our model with that in Prakash's study. In our model, EMT-transitioning cells are identified by their EMT marker genes and fluorescence expression. We enriched the EMT transitioning cells by sorting the Doub+ cells. Due to the RFP protein's half-life, cells remain RFP+ for 2-3 days after the reporter cassette has switched to GFP expression. In Prakash's study, the EMT transitioning phase was defines by the duration of TGF-β stimulation.

In Figure 1K, cells are categorized based on their EMT pseudotime, calculated from their expression of EMT marker genes in the EMTome. Ribosome biogenesis (RiBi) activity is highest in cells transitioning between phase 1 (Red) and phase 2 (Green), with both phases displaying predominantly epithelial phenotypes (Figures 1C, 1D, and 1E). RiBi activity declines in cells in phases 4, 5, and 3, which exhibit a mesenchymal phenotype. We have expanded the discussion to include more details in comparison with Prakash's study in the revised manuscript.

Supp Fig S4. The authors should provide a rationale for how and why the specific marker genes were selected to calculate the AUC values. 

We have chosen the specific EMT marker genes based on their overall expression levels in Tri-PyMT cells, ensuring consistency with the reported associations of their expression patterns to epithelial or mesenchymal phenotypes in the literature. We provide a detailed rationale for the selection of these genes in the Method of revised manuscript (Page #7).

Figure 2 and associated supplementary figure panel. In this figure, rRNA synthesis needs to be evaluated in the cells isolated from the lungs to corroborate the RNA sequencing findings. 

Following the reviewer’s suggestion, we performed an RT-PCR of Ribi related genes including Bop1, Gemin4, Its1, Its2, Npm1, Rpl8, Rpl29, Rps9, Rps24, Rps28, Polr1a, Setd4, Utp6, and Xpo1. Consistent with the bulk and single cell RNA sequencing, relatively higher expression of Ribi related genes were detected in Doub+ cells compared to that of RFP+ and GFP+ cells (revised Supplementary Fig S5). 

Fig 2C, as per figure Supp Fig S4 please explain the rationale for how and why the specific marker genes were selected. 

The same marker genes used for the calculation of the EMT AUC value as in Fig. 1. These marker genes were selected because their overall expression levels are readily detectable in Tri-PyMT cells, their expression patterns are consistent with their epithelial or mesenchymal phenotypes, and the associations between expression of marker genes and phenotypes are in line with the previous reports in literature. Description of AUCell value quantification was included in the revised manuscript (Page #7).

Fig. 2G. The high Ribi during the epithelial state is most likely due to the resumption of cell proliferation of these cells. The authors should check the cell cycle states of these different sets of cells. 

We agree with the reviewer that higher Ribi activity could be related to the resumption of cell proliferation of mesenchymal tumor cells. To clarify this, we revisited the scRNAseq data, and project the S phase score to the scatter plot of Ribi activity/MET pseudotime. Indeed, cells in the far mesenchymal state show low S phase score, while the proliferating cells were mostly detected in the MET transitioning phase and epithelial phase (revised Supplementary Figure S6D).

Suppl Fig. 5 Please correct the figure legends as there is no figure D. 

We apologize for the mislabeling. We have corrected the figure legend accordingly.

Figure 3. Please explain the rationale for stimulating cells with FBS for the selected time points. 

Fig. 3A. The loading control is not even, and quantification is missing. In addition, the authors should explain why the different time points were chosen and why FBS was chosen as a stimulus. In addition, from which passage of cells were these cells? 

The RFP+ Tri-PyMT cells underwent EMT and switched their expression of fluorescent marker to GFP+ when cultured with FBS. To investigate the response of cells at varying EMT statuses to an FBS-enriched environment, we isolated RFP+, Doub+, and GFP+ cells from the 4th and 5th passages of Tri-PyMT cells and probed downstream signaling pathways after FBS stimuli. The timeline for stimulation was informed by the innate activation profile of these phosphorylation-dependent signals, spanning from 10 minutes to 1 hour. We noted that ERK signaling activation in RFP+ cells occurred within minutes of FBS exposure and diminished within approximately one hour. This ERK signal was more pronounced and persisted longer in Doub+ cells. In contrast, GFP+ cells exhibited a more transient and lower ERK activation (see revised Fig 3A). To address concerns regarding potential uneven loading in our previous assays, we have now included the quantification of Western blots in the revised Fig 3A.

How and why were ERK and mTORC1 pathways chosen for analysis downstream of increased rRNA synthesis? ERK and mTORC1 have mostly been investigated in the role of cell proliferation which is why the cell cycle status of these cell populations will be important to consider in the context of their findings. 

The regulation of ribosome biogenesis (RiBi) is mediated by multiple pathways, including the myelocytomatosis oncogene (Myc), mammalian targets of rapamycin (mTOR), and noncoding RNAs, as detailed by Jiao et al. in Signal Transduction and Targeted Therapy (2023). There was no significant difference in Myc expression between tumor cells with epithelial and mesenchymal phenotypes. We thus investigated the activation of the mTOR pathway in sorted RFP+, Doub+, and GFP+ cells. Additionally, given the recognized role of the ERK/MAPK signaling pathway in regulating protein synthesis and cell proliferation, we also analyzed the activation of ERK signals. 

In alignment with the reviewer's observation regarding the potential correlation between cell proliferation rate and RiBi activation, we further characterized the cell cycle distributions of RFP+, Doub+, and GFP+ cells. Notably, the Doub+ cells exhibited a higher ratio of cells in the proliferative state (including S and G2/M phases) compared to RFP+ and GFP+ cells. Also, higher percentage of S phase cells were detected in RFP+ cells than GFP+ cells (revised Supplementary Figure S1B).

Figure 3 B, C, D. Please provide more information about which cells are analyzed in this figure. 

We apologize for the previous ambiguity regarding the cells analyzed in these figures. To clarify, the figure legend has been revised to specify that Tri-PyMT cells from the 5th to 10th passages were the subjects of analysis for cell size and nascent protein synthesis, utilizing flow cytometry.

Figure 3D. The selected images show enlarged nucleoli/ fibrillarin which is an indicator of increased rRNA synthesis however, the authors need to show an increase in rRNA transcripts by q-PCR or Northern blot and also show EU staining in these different cell states to support their claim. 

We appreciate the reviewer's recommendation to further validate the enhanced ribosome biogenesis (RiBi) in Doub+ cells. In response, we conducted RT-PCR analysis of several RiBi-related genes (revised Supplementary Fig S5). Additionally, we carried out an EU incorporation assay to illustrate the rRNA transcription activity within these cells. The new results have been incorporated into the revised manuscript (Supplementary Fig S7).

Figure 4 and associated supplementary. In this figure, the authors show that using small molecule Pol I assembly inhibitors (BMH-21 and CX-5461) reduces the expression of mesenchymal proteins. As mentioned in previous comments these results should be put in the context of published work by Prakash et al which demonstrate that upon CX-5461 and genetic silencing of Pol I EMT is hampered as demonstrated by gene expression profiles as well as functional assays. 

We revised the description of our experiments with Pol I inhibitors in the revised manuscript by including the citation context (Prakash et al Nat Commun, 2019) as mentioned above.  

Figure 4A. Please provide an explanation of how the doses of Pol I assembly inhibitors were determined and also the selected time points. The Pol I assembly inhibitors should have an effect within a few hours (Drygin, Cancer Research, 2011, Peltonen, Cancer Cell, 24). The authors also need to show that the BMH-21 and CX5461 at selected doses are indeed inhibiting rRNA synthesis in the selected cell populations. The data would also be strengthened by performing ChIP analysis demonstrating that indeed the Pol I complex is disassociated from the rDNA genes upon inhibition. 

In addition, why are there only 2 reports and how were the statistics done? Were the data normalized to the total number of cells? The graph visually shows a difference in cell numbers. Are cells dying at this concentration? More controls must be included including markers for cell stress, p53, autophagy, and apoptosis. 

The dose of Pol inhibitors was selected based on prior studies, as noted by the reviewer. Peltonen et al. demonstrated that BMH-21 inhibits growth across a wide spectrum of cancer cell lines, achieving a mean half-maximal inhibition of cell proliferation (GI50) at 160 nM (Peltonen K., et al. Cancer Cell. 2014). Consistently, in our experiments, the growth inhibitory effect of BMH-21 on Tri-PyMT cells fell within this range, at approximately 200 nM (Fig 5B, Supplementary Fig S10). 

To address the reviewer's suggestion and verify that RiBi inhibitor effectively inhibits rRNA synthesis in our study, we conducted an EU incorporation assay. This assay revealed significant inhibition of rRNA synthesis by BMH-21 and CX5461 in Tri-PyMT cells (revised Supplementary Fig S8B). Furthermore, to enhance the robustness of our findings, we repeated the BMH-21 treatment on sorted RFP+ Tri-PyMT cells across three biological replicates, which yielded consistent results.

Figure 4B. How many replicates were done for this experiment and please provide quantification as per previous comments on WB experiments. The authors should provide a rationale for why Snail and Vimentin were chosen for these studies. Also, the authors should provide a functional assay and demonstrate that cells are less migratory post-treatment and not only markers. 

Western blots with sorted Tri-PyMT cells were performed twice. We have added the quantification of these blot in the revised manuscript. Snail and Vimentin were chosen as mesenchymal markers to indicate EMT phenotype switches as those were well-studied and commonly used mesenchymal markers of EMT. The association of fluorescent marker switch and

EMT phenotype such as cell migration was well established in our previous study (Fischer et al., 2015, Lourenco et al., 2020). The morphology and migration property of GFP+ were well distinguished from RFP+ counterparts. Also, following reviewer’s suggestion, we performed migration assay with BMH21 treatment (revised Supplementary Fig 8C). Indeed, the treatment with BMH21 or CX5461 inhibited cell migration as expected.

Supplementary figure 7. The authors need to provide a rationale as to why the two Rps were chosen to inhibit ribosome biogenesis. 

The two Rps targets were chosen based on their differential expression in Doub+ cells compared with RFP+ and GFP+ cells. Also, we considered the overall expression level of these genes in Tri-PyMT cells. We have edited the according text in the revised manuscript.

Figure S7B. In the images shown there does not appear to be a significant change in the number of nucleoli however the cells seem to be smaller. This should be explained. 

We agree with the reviewer that the box plot does not clearly show the nucleoli differences between these cells. We present the data with a violin plot, which more clearly exhibit the result (revised Supplementary Fig S9B). It was also true that the sizes of the Rps knockdown cells were relatively smaller than control cells. This is consistent with the finding that the EMT transitioning cell size was bigger than the non-transitioning cells (Fig 3B)

.

Figure 5 and Supp 8. The authors should provide the background as to why the specific chemotherapeutic drugs were chosen. 

The chemotherapeutic agents employed in this study are widely used in the treatment of breast cancer. For instance, Cyclophosphamide (CTX) hampers both DNA replication and RNA transcription; Doxorubicin inhibits DNA replication by disrupting topoisomerase activity; Paclitaxel prevents cell division by stabilizing microtubules; and 5-Fluorouracil (5-FU), a pyrimidine analog, blocks thymidylate synthase, thereby disrupting DNA synthesis. Additionally, some of these agents, such as CTX and 5-FU, may directly or indirectly affect RNA polymerase, prompting us to investigate the synergistic effects of these drugs when used in combination with BMH21. We have included the information in revised manuscript. 

Fig 5B/Supp 8. Can the authors please explain why only 2 replicates were done and provide a rationale for future statistics? 

Using serial concentrations of drugs tested—6 doses for BMH21 and 8 doses for CTX—it is logical to arrange the experiment in duplicates on 96-well plates. For the statistical analysis, we conducted dose-response analysis to ascertain the IC50 values for each drug alone and in combination. Additionally, we calculated the synergy score to assess the interactions between the drugs. The methodology section of the manuscript has been enhanced to provide a clearer description of these processes in the revised version.

Figure 6. The authors should provide a rationale of why tail veins were chosen as their in vivo model system as the EMT cells do not cause metastasis and if chemoresistance is the main focus of their studies both primary and secondary tumors should be considered. Why was not the MMTVPyMT mouse model chosen where the cells were originally isolated from to test the role of the dual treatment? How was the drug concentration decided and the interval of treatments? 

We acknowledge the reviewer's concerns regarding the choice of experimental setup for our metastasis model. Certainly, utilizing the original MMTV-PyMT mice for the combination therapy experiment would be the ideal scenario. However, there are potential drawbacks to using these transgenic mice: 1) The occurrence of multiple primary tumors that develop simultaneously but without synchronized timelines (in mice aged 6-9 weeks), and the unsynchronized development of lung metastasis (from 10-16 weeks of age). This leads to uncontrollable variations in the experimental setup, particularly when establishing multiple treatment groups; 2) Gathering a sufficient number of female transgenic mice of a similar age poses another challenge; 3) The absence of tumor cell labeling complicates the focus on assays for EMT/MET phenotype changes during tumor progression. Consequently, we have chosen to employ our Tri-PyMT model for this experiment. The drug treatment protocol was established after reviewing literature on the in vivo application of CTX and BMH21 treatment (Peltonen etal. Cancer Cell 2014; Jacobs etal. JBC 2022).

Figure 6B, C. The authors should provide quantification for these data, how many mice were analyzed, and how many sections were stained and analyzed. 

We have improved the quality of these fluorescent images and clarify the methodology, including the mouse/section numbers per group, for obtaining these fluorescent images in the legend. To quantify the differential impact of BMH21 on RFP+ and GFP+ tumor cells, we performed flow cytometry (revised Supplementary Fig S11). We have also changed the presentation of these flow data to improve the clarity of these results. 

Fig 6D. How were the treatment timeline and dosing chosen? LM2 cells are derived from a metastatic site, so they are not transitioning cells they are stably mesenchymal why was this chosen as their in vivo model? 

LM2 cells were derived from the lung metastasis of MDA-MB-231 cell line. These cells exhibit predominantly mesenchymal phenotype in culture. While growing into metastasis in the lung, expressions of epithelial markers such as E-cad were upregulated (Supplementary Fig S12), suggesting a MET process may be involved the outgrowth of lung metastasis. Therefore, we choose the LM2 cells as our experimental model for assessing the effect of RiBi inhibitor on MET. The treatment timeline was determined based on previous studies of BMH21 and chemotherapy applications in vivo (Peltonen etal. Cancer Cell 2014; Jacobs etal. JBC 2022).  

Reviewer #3 (Public Review): 

Summary: 

Ban et al. investigated the role of ribosome biogenesis (RiBi) in epithelial-to-mesenchymal transition (EMT) and its contribution to chemoresistance in breast cancer. They used a Tri-PyMT EMT lineage-tracing model and scRNA-seq to analyze EMT status and found that RiBi was elevated during both EMT and mesenchymal-to-epithelial transition (MET) of cancer cells. They further revealed that nascent protein synthesis mediated by ERK and mTOR signaling pathways was essential for the completion of RiBi. Inhibiting excessive RiBi impaired EMT and MET capability. More importantly, combinatorial treatment with RiBi inhibitors and chemotherapy drugs reduced metastatic outgrowth of both epithelial and mesenchymal tumor cells. These results suggest that targeting the RiBi pathway may be an effective strategy for treating advanced breast cancer with EMT-related chemoresistance. 

Strengths: 

The conclusions of this study are generally supported by the data. However, some weaknesses still exist as mentioned below. 

Weaknesses: 

(1) The study predominantly focused on RiBi as a target for overcoming EMT-related chemoresistance. Thus, it will be necessary to provide some canonical outcomes after upregulating ribosome biogenesis, such as translation activity. I would suggest ribosome profiling or puromycin-incorporation assay, or other more suitable experiments. 

EU incorporation assay (revised Supplementary Fig S7) and puromycin incorporation assay (Fig 3C) were performed.

(2) The results were basically obtained from mice and in vitro experiments. While these results provide valuable insights, it will be valuable to validate part of the findings using some tissue samples from patients (e.g. RiBi activity) to determine the clinical relevance and potential therapeutic applications.  

We agree. We have added the analyses on the correlation between patients’ survival and RiBi activation (revised Supplementary Fig S13, S14).

(3) The results revealed that mTORC1 and ERK mediated RiBi activation. How about mTORC2? It will be informative to evaluate mTORC2 signaling. 

We investigated the role of the mTORC1 pathway in regulating RiBi activation. It is pertinent to acknowledge that the mTORC1 complex is known to positively regulate protein synthesis through the phosphorylation of ribosomal protein S6 kinase, among other mechanisms. Additionally, Rps6 is recognized as an essential component of the 40S subunit in the ribosome. We agree with the reviewer that mTORC2 may also be involved in RiBi activity, as its activation is mediated through ribosome association (Zinzalla et al., Cell 2011; Prakash et al., Nat Comm 2019). However, this association is more likely to be downstream of RiBi activation, as the RiBi inhibitor CX5461 can block the translocation of Rictor into the nucleus (Prakash et al., Nat Comm 2019).

We also revisited our sequencing data of RFP+, GFP+, and Doub+ cells. While there was no significant change in the expression of either Rptor or Rictor among these cells, the LSMean (overall expression level) of Rptor was higher than that of Rictor; for example, 163.77 vs 29.95 in RFP+ cells. This suggests that mTORC1 may play a dominant role in regulating RiBi activity in our model.

Furthermore, we analyzed how Rapamycin (an mTORC1 inhibitor) affects the EMT process in TriPyMT cells. As expected, Rapamycin-treated cells exhibited higher expression of the epithelial marker E-cadherin (Ecad) and lower expression of the mesenchymal markers Snail and Vimentin (Vim) compared to the control (For Reviewers Figure 3).

(4) The results also demonstrated promising synergic effects of Pol I inhibitor (BMH21) and chemotherapy drug (CTX) on chemo-resistant metastasis. How about using the inhibitors of mTORC1 together with CTX? 

Several mTOR inhibitors (e.g., sirolimus, temsirolimus, ridaforolimus) have demonstrated antitumor activity. The combination of mTOR inhibitors with various targeted therapies or chemotherapies is being examined in numerous clinical trials, showing promising results. Although the combination therapy of mTORC inhibitors and CTX is beyond the scope of our study, we analyzed how mTOR inhibitors may affect the EMT process in our model, as mentioned above. Western blot analysis of EMT markers (E-cadherin, Snail, and Vimentin) showed that rapamycin treatment inhibited the EMT transition of Tri-PyMT cells. (For Reviewers Figure 3).

(5) While the results demonstrate the potential efficacy of RiBi inhibitors in reducing metastatic outgrowth, other factors and mechanisms contributing to chemoresistance may exist and need further investigation. I would suggest some discussion about this aspect. 

Following reviewer’s suggestion, we have edited the discussion section with more future directions. 

Reviewer #3 (Recommendations For The Authors): 

(1) Please provide the quantified data for all western blots, rather than solely show some representative blots. 

We quantified the western blot images as shown in the revised figures. Thanks for reviewer’s suggestion.  

(2) Please add a graphic abstract or schematic to help the readers understand the whole story. 

We have summarized a schematic graph of our findings in the revised manuscript (Supplementary Fig S15).

(3) It is hard to read the numbers inside all plots of flow cytometry. 

High-resolution figures of flow plots are included in the revised manuscript.

(4) Please provide high-resolution figures for all the synergy plots.

High-resolution figures of synergy plots are included in the revised manuscript.

eLife assessment

This fundamental study identifies the kinase DYRK1A as a novel component of the tuberous sclerosis complex (TSC) protein complex, which is central to cellular growth and cell size. The findings presented here have broad implications for how cell size and growth is regulated. The methodology and analysis are convincing and support the findings.

Reviewer #2 (Public Review):

This study reports a physical interaction between the kinase DYRK1A and the Tuberous Sclerosis Complex (TSC) protein complex (TSC1, TSC2, TBC1D7). Furthermore, this study demonstrates that DYRK1A, upon interaction with the TSC proteins, regulates mTORC1 activity and cell size. Additionally, this study identifies T1462 on TSC2 as a phosphorylation target of DYRK1A. Finally, the authors demonstrate that DYRK1A impacts cell size using human, mouse and Drosophila cells.

The interaction described here is highly impactful to the field of mTORC1-regulated cell growth and uncovers a previously unrecognized TSC-associated interacting protein. DYRK1A and its regulation of mTORC1 activation may have an impact for multiple diseases in which mTORC1 is hyperactivated.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

In this manuscript, Wang et al. demonstrate that knockdown of DYRK1A results in reduced cell size, which is mediated by mTORC1 activity. They found that DYRK1A interacts with TSC1/TSC2 proteins which leads to the phosphorylation of TSC2 at T1462. Phosphorylation of TSC2 at T1462 inhibits TSC2 activity leading to the activation of mTORC1. The authors complement their findings by demonstrating that overexpression of RHEB (positive regulator of mTORC1) rescues the phenotype of DYRK1A (mnb in flies) mutation in the NMJ.

The authors' findings on the regulation of cell size and mTORC1 activity by DYRK1A reflect the previous findings of Levy et al. (PMID: 33840455) that cortical deletion of Dyrk1a in mice causes decreased neuronal size associated with a decreased activity of mTORC1 that can be rescued by the inhibition of Pten or supplementation of IGF1.

The authors demonstrate that T1462 phospho-site at TSC2 is phosphorylated in response to the overexpression of WT but not kinase-dead DYRK1A. However, the authors do not provide any evidence that the regulation of mTORC1 is mediated via phosphorylation of this site. In addition, T1462 site is known to be phosphorylated by Akt. There is a possibility that Akt was co-purified with TSC1/TSC2 complex and DYRK1A promotes phosphorylation of TSC2 indirectly via the activation of AKT that can be tested by using AKT depleted cells.

We thank the reviewer for reviewing this manuscript and the critical comments. Various groups have reported the significance of the Phosphorylation of TSC2 T1462, along with four other phosphorylation sites, in regulating mTORC1, and therefore, we did not deal with this in the current manuscript (Manning et al. PMID: 12150915, Inoki et al. PMID: 12172553, Zhang et al. PMID: 19593385). Regarding co-purification of AKT with TSC1/TSC2 - AKT phosphorylates T1462, S939 and S1387 (Manning et al. PMID: 12150915, Inoki et al. PMID: 12172553, Zhang et al. PMID: 19593385). However, in in vitro kinase assay, signal intensities of anti-TSC2 S939 and S1387, with or without ATP, showed no significant difference, suggesting that AKT is not pulled down with TSC1 or TSC2. DYRK1A and Kinase dead DYRK1A were expressed and purified from bacteria.  Moreover, multiple studies have purified TSC1 and TSC2 and reported no AKT co-purified (Menon et al. PMID: 24529379, Chong-kopera et al. PMID: 16464865).

RHEB is the most proximal regulator of mTORC1 and can activate mTORC1 even under amino acid starvation. The fact that RHEB overexpression rescues the cell size under DYRK1A depletion or mnb (DYRK1A in Drosophila) mutant phenotype does not prove that DYRK1A regulates the cell size via TSC1 as it would rescue any inhibitory effects upstream to mTORC1.

We agree with the reviewer that overexpression of RHEB may rescue any inhibitory effects upstream to mTORC1.  In the results and discussion sections (Page number 7, last 3 lines), we mentioned that Rheb overexpression only supports our suggestion that DYRK1A likely works upstream to RHEB. We, however, have performed another experiment to strengthen our hypothesis. We show that increased cell size phenotype due to DYRK1A overexpression can be suppressed by inhibiting the TORC1 pathway, suggesting that mTORC1 is necessary for DYRK1A-mediated cell growth.  These results are presented in Supplementary Figure 4. The results of two reciprocals of experiments (Suppression of DRYK1A/Mnb loss of function phenotypes by RHEB overexpression and suppression of rescue of DYRK1A Gain of function phenotypes) along with and regulation of TSC phosphorylation by DYRK1A strongly suggests that DYRK1A positively regulates TSC pathway.

Reviewer #2 (Public Review):

This study aims to describe a physical interaction between the kinase DYRK1A and the Tuberous Sclerosis Complex proteins (TSC1, TSC2, TBC1D7). Furthermore, this study aims to demonstrate that DYRK1A, upon interaction with the TSC proteins regulates mTORC1 activity and cell size. Additionally, this study identifies T1462 on TSC2 as a phosphorylation target of DYRK1A. Finally, the authors demonstrate the role of DYRK1A on cell size using human, mouse, and Drosophila cells.

This study, as it stands, requires further experimentation to support the conclusions on the role of DYRK1A on TSC interaction and subsequently on mTORC1 regulation. Weaknesses include, 1) The lack of an additional assessment of cell growth/size (eg. protein content, proliferation), 2) the limited data on the requirement of DYRK1A for TSC complex stability and function, and 3) the limited perturbations on the mTORC1 pathway upon DYRK1A deletion/overexpression.

We thank the reviewer for reviewing this manuscript and the comments. We have previously analyzed the effect of DYRK1A knockdown in the proliferation of THP cells (human leukemia monocytic cell line) (Li Shanshan et al. PMID: 30137413) and have shown that DYRK1A knockdown negatively affects cell proliferation. Other studies have also shown a role for DYRK1A in cell proliferation, including in foreskin fibroblasts (Chen et al. PMID: 24119401) and HepG2 cells (Frendo-Cumbo et al. PMID: 36248734). mTORC1 regulates several pathways, including protein synthesis, lipid synthesis, nucleotide synthesis, autophagy, and stress responses. We have not done the protein content as this parameter is directly affected by TORC1 activation and may not be a suitable measure for cell growth. A large number of studies involving mTORC1 regulation analyze the levels of S6K and S6 phosphorylation, as these are direct readouts of mTORC1 function   (Prentzell et al. PMID: 33497611,  Zhang et al. PMID: 17052453, Ben-Sahra et al, PMID: 23429703, Düvel et al. PMID: 20670887,  Zhang et al. PMID: 2504303). Therefore, we used these markers to assess the status of the mTORC1 pathway.

(2) ..the limited data on the requirement of DYRK1A for TSC complex stability and function,

We agree with this limitation in our study. We have not seen a significant difference in TSC1 or TSC2 protein levels in DYRK1A knockdown or overexpressing cells, so we did not follow up on this aspect.

..and 3) the limited perturbations on the mTORC1 pathway upon DYRK1A deletion /overexpression.

We have performed an additional experiment where we overexpressed DYRK1A and showed that increased cell size phenotype due to DYRK1A overexpression can be suppressed by inhibiting the TORC1 pathway, suggesting that mTORC1 is necessary for DYRK1A-mediated cell growth.  These results are presented in Supplementary Figure 4. The results of two reciprocals of experiments (Suppression of DRYK1A/Mnb loss of function phenotypes by RHEB overexpression and suppression of Rescue of DYRK1A Gain of function phenotypes) along with and regulation of TSC phosphorylation by DYRK1A suggests that DYRK1A positively regulates TSC pathway.

Finally, this study would benefit from identifying under which nutrient conditions DYRK1A interacts with the TS complex to regulate mTORC1. The interaction described here is highly impactful to the field of mTORC1-regulated cell growth and uncovers a previously unrecognized TSC-associated interacting protein. Further characterization of the role that DYRK1A plays in regulating mTORC1 activation and the upstream signals that stimulate this interaction will be extremely important for multiple diseases that exhibit mTORC1 hyper-activation.

We agree that identifying nutrients (or physiological conditions) that affect DYRK1A-mediated TSC regulation will be important to understanding the additional complexity in context-dependent mTORC1 activation/deactivation. This study has not addressed those issues, particularly due to DYRK1A's pleiotropic nature. DYRK1A has many substrates, and both overexpression and loss of DYRK1A lead to multiple phenotypes. Identifying nutrient conditions or growth factors that can regulate the activation of DYRK1A is not yet known and would require an independent investigation.

Reviewer #3 (Public Review):

The manuscript describes a combination of in vitro and in vivo results implicating Dyrk1a in the regulation of mTORC. Particular strengths of the data are this combination of cell and whole animal (drosophila) based studies. However, most of the experiments seem to lack a key additional experimental condition that could increase confidence in the authors' conclusions. Overall some tantalizing data is presented. However, there are several issues that should be clarified or otherwise addressed with additional data.

We thank the reviewer for reviewing and commenting on this manuscript.

(1) In Figure 1G, why not test overexpression levels of Dyrk1a via western rather than only looking at the RNA levels?

Induced overexpression of DYRK1A was probed by analyzing mRNA levels, as the concentration of Doxycycline used (0-100 ng/ml) did not produce enough protein that could be detected by anti-flag antibody in a western blot. We have modified the sentence (page 5, paragraph 1).

(2) In Figure 2, while there is clearly TSC1 protein in the Dyrk1a and FLAG-Dyrk1a IPs that supports an interaction between the proteins, it would be good to see the reciprocal IP experiment wherein TSC1 or TSC2 are pulled down and then the blot probed for Dyrk1a.

In the revised manuscript, we have provided evidence that TSC1 and TSC2 can interact with endogenous DYRK1A. We have performed immunoprecipitation of affinity-tagged TSC1 or TSC2 and have probed for the enrichment of DYRK1A (Supplementary Figure S2).

(3) Figures 3 A and D tested the effects of Dyrk1a knockdown using different methods in different cell lines. This is a reasonable approach to ascertain the generalizability of findings. However, each experiment is performed differently. For example, in 3A, the authors found no difference in baseline pS6, so they did a time course of treatment to induce phosphorylation and found differences depending on Dyrk1a expression. In 3D, they only show baseline effects from the CRISPR knockdown. Why not do the time course as well for consistency? Also, why the an inconsistency in approaches wherein one shows baseline effects and the other does not? The authors could also consider the pharmacologic inhibition of Dyrk1a activity as well.

We agree that different methods were used in different cell lines to assess the effect of DYRK1A. Since DYRK1A is a pleiotropic gene, its manipulation has diverse effects on different cell lines. Also, not all cell types have similar levels of mTORC activity. Hence, we had to adapt to different strategies in different cell types, which accounted for the inconsistency in the methodology.  However, various groups have used these methods to determine the activity of mTORC1 by S6 and S6K phosphorylation by both starvations, followed by the stimulation and direct estimation methods in cycling cells (Prentzell et al. PMID: 33497611,  Zhang et al. PMID: 17052453, Ben-Sahra et al, PMID: 23429703, Düvel et al. PMID: 20670887,  Zhang et al. PMID: 25043031). ShRNA-mediated knockdown in HEK293 cells does not change S6 or S6K phosphorylation levels in actively growing cells, whereas cycling NIH3T3 cells shows a significant reduction in S6 and S6K phosphorylation. As suggested, we used pharmacological inhibition of DYRK1A and 1uM Harmine to treat the HEK293 cells and perform starvation. However, cells treated and starved start to float and die in large numbers. Thus, we did not follow this experiment further.

(4) In Figure 4, RHEB overexpression increases cell size in both Dyrk1a wt and Dyrk1a shRNA treated cells, although the magnitude of the effect appears reduced in Dyrk1a shRNA cells. However, there is the possibility here that RHEB acts independently of Dyrk1a. Why not also do the experiment of Figure 1 wherein Dyrk1a is overexpressed and then knockdown RHEB in that context? If the hypothesis is supported, then RHEB knockdown should eliminate the cell size effect of Dyrk1a overexpression.

We thank the reviewer for suggesting this experiment.  We have overexpressed DYRK1A using the inducible HEK293A-Flag-DYRK1A overexpression system and treated cells with mTOR inhibitors (Rapamycin or Torin1). The results are added to the supplementary figure S4. Our results show that the increased cell size phenotype due to DYRK1A overexpression can be suppressed by inhibiting the TORC1 pathway. This suggests that mTORC1 is necessary for DYRK1A-mediated cell growth. This data further supports the hypothesis that DYRK1A is a positive regulator of the mTORC1 pathway.

(5) The discussion should incorporate relevant findings from other models, such as Arabidopsis. Barrada et al., Development (2019), 146 (3).

We have incorporated the findings from Arabidopsis (Barrada et al., Development (2019), 146 (3) PMID: 30705074) in the last paragraph of the discussion section.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) To demonstrate that DYRK1A can phosphorylate T1462 phospho-site at TSC2 in the absence of Akt using genetic and pharmacological approaches (by using pan-Akt small molecule inhibitors).

We have performed in vitro kinase assay using recombinant DYRK1A, and affinity purified TSC1/TSC2 from HEK293 cells. However, we have not been able to perform this experiment by overexpression of DYRK1A in human cells, as 1) strong overexpression of DYRK1A leads to cell cycle exit, as demonstrated by various laboratories (Soppa et al. PMID: 24806449, Hämmerle et al PMID: 21610031,  Najas et al. PMID: 26137553, Park et al. PMID: 20696760) and our observations, and 2) T1462 Antibody signal is weak and cannot be seen in cellular extracts. We have attempted this experiment with at least three different batches of T1462 antibody from CST without success.

(2) To demonstrate that endogenous phosho-mutant/mimetic substitution of T1462 phospho-site at TSC2 is sufficient to prevent the regulation of cell size/NMJ phenotype in Drosophila by DYRK1A (mnb).

This is an interesting experiment, and we thank the reviewer for this suggestion. However, we are skeptical about interpreting the possible results. Since T1462 substitution will also block the regulation by other kinases, e.g., Akt, and it may constitutively suppress the mTORC1, any interpretation will be confusing.

Reviewer #2 (Recommendations For The Authors):

(1) In section 2.1 the authors claim that DYRK1A down-regulation enhances cell growth. An additional assessment of cell growth or size would strengthen this statement. Is total protein content also increased upon DYRK1A overexpression? Does DYRK1A KD also increase cell proliferation? In Figure 1, providing the median or mean size of cells in each condition will help the reader understand the impact of DYRK1A on cell size. In Supplementary Figure 1, the important statistical differences should be highlighted.

We have not claimed that down-regulation of DYRK1A enhances cell growth. We have not tested the protein content in a cell directly. Knockdown of DYRK1A leads to a reduction in cell proliferation, as shown by various groups, including ours (Shanshan Li PMID: 30137413, Luna et al. PMID: 30343272). Cell size is a very dynamic process and is variable within the population. All the studies measuring cell size show the size using assays on a population of cells. We have not been able to figure out a way to display the median or mean cell size that accurately reflects the cell size of the whole population. 

(2) In section 2.2 the authors describe the interaction between DYRK1A and the TSC proteins. Do the DYRK1A mutants impact interaction with TSC2 and TBC1D7 or is this specific to TSC1?

We have not tested this possibility.

(3) In section 2.3, more detailed perturbations of the mTORC1 pathway are needed. Is the mTORC1 activation observed sensitive to rapamycin treatment? Since mTORC1 regulates cell size via S6 ribosomal protein and transcription via 4EBP1, phosphorylation of 4EBP1 should also be considered. In Figure 3A, what is the level of DYRK1A down-regulation? It is unclear how many shRNA constructs were used or whether these were pooled constructs or single clones. If one shRNA/sgRNA is used, it would be very helpful to validate some of the key findings of this study with at least one more clone.

Many research studies have measured the activity of various mTORC1 substrates, the most commonly used being the phosphorylation of S6 and S6K. We agree that analyzing 4EBP1 would make the study more comprehensive, but to complete the study with our limited resources and in a limited time, we have not attempted to establish the 4EBP1 phosphorylation status. We have used a previously described and validated DYRK1A shRNA (as mentioned in the methods section).

(4) In section 2.3 is T1462 an activating or inhibiting phosphorylation event? If DYRK1A phosphorylates and activates mTORC1 via RHEB, shouldn't that result in the inhibition of mTORC1?

Multiple laboratories have demonstrated that T1462 phosphorylation leads to a reduced TSC complex activity and, hence, increased mTORC1 activity (Manning et al. PMID: 12150915, Inoki, PMID: 12172553, Zhang PMID: 19593385).

(5) In section 2.4, what is the status of AKT phosphorylation? Would an AKT inhibitor be useful in this scenario?

AKT phosphorylates T1462, S939 and S1360, as demonstrated by others. However, in our in vitro assay kinase assay, the following facts suggest that AKT is not involved in T1462 phosphorylation we observed:

(1) Signal intensities of anti-TSC2 S939 and S1387 with or without ATP, do not show any significant differences, suggesting that AKT is not pulled down with TSC1 or TSC2.

(2) Multiple studies have performed phosphorylation studies of TSC1 and TSC2 and have not reported any co-purification of AKT.

(6) Very minor grammar errors were observed, mostly at the beginning of the manuscript.

We tried our best to fix grammatical errors.

Author response:

Reviewer #1 (Public Review):

In this manuscript, Yang et al. conduct a comprehensive investigation to demonstrate the role of adipose tissue Mir802 in obesity-associated inflammation and metabolic dysfunction. Using multiple models and techniques, they propose a mechanism where elevated levels of Mir802 in adipose tissue (both in mouse models and humans) trigger fat accumulation and inflammation, leading to increased adiposity and insulin resistance. They suggest that increased Mir802 levels in adipocytes during obesity result in the downregulation of TRAF3, a negative regulator of canonical and non-canonical NF-κB pathways. This downregulation induces inflammation through the production of cytokines/chemokines that attract and polarize macrophages. Concurrently, the NF-κB pathway induces the lipogenic transcriptional factor SREBP1, which promotes fat accumulation and further recruits pro-inflammatory macrophages. While the proposed model is supported by multiple experiments and consistent data, there are areas where the manuscript could be improved. Some improvements can be addressed in the text, while others require additional controls, experiments, or analyses.

1) The manuscript should provide measurements of lipid droplet/adipocyte size for all models, both in vitro and in vivo. In vivo studies should also include fat weight measurements. This is crucial to determine whether Mir802, TRAF3, and SREBP1 promote adiposity/fat accumulation across all models.

Thank you for your careful reviewing. As suggested, we have measured the size of lipid droplet and adipocyte (1J, 2A, S2I, 3F, 3L, S3L, 5I), this modification can make you and other readers understand our manuscript more clearly. In vivo studies have included fat weight measurements (Figure 2K, L; Figure 3C, D; Figure 5N). Our results determined that adipose-selective overexpression Mir802 induced adipogenesis during high fat diet induced.

2) The rationale for co-culture experiments using WAT SVF is unclear, given that Mir802 is upregulated by obesity in adipocytes, not in the stromal-vascular fraction. These experiments would be more relevant if performed using isolated adipocytes or differentiated WAT SVF.

Thank you for this important point. We are sorry for our inaccurate expression. In our study, we used differentiated WAT SVF to co-culture with primary macrophage, we illustrated it in the methods of Migration and invasion assays. We have revised it in the Flowchart of the co-culture experiments (Figure 4A). We hope that this modification will enhance readers' comprehension of our manuscript.

3) Figures 1G and 1H lack a control group (time 0 or NCD). Without this control, it is impossible to determine if inflammation precedes Mir802 upregulation.

Thank you for this insightful comment. In the previous study, we have tested the 0 weeks high fed diet treatment group of the Figures 1I and 1J, now we have added this data in the manuscript, we hope this modification can enhance our conclusion that inflammation precedes Mir802 upregulation.

4) The statement, "The knockout of Mir802 in adipose tissue did not alter food intake, body weight, glucose level, and adiposity (data not shown)," needs more detail regarding the age and sex of the animals. These data are important and should be reported, perhaps in a supplementary figure.

Thank you for your careful reviewing. To enhance our conclusions, we have added the data of food intake, body weight, glucose level, and adiposity about Mir802 KO mice treated with normal chow diet (NCD, Supplementary Figure 3E-I).

….The knockout of Mir802 in adipose tissue did not alter food intake, body weight, glucose levels, and adiposity compared with their WT littermates in both males and females when they were fed with NCD (Figure S3E-I)……

5) The terms "KO" (knockout) and "KI" (knock-in) are misleading for AAV models, as they do not modify the genome. "KD" (knockdown) and "OE" (overexpression) are more accurate.

Thank you for your good advice. We are sorry for our inaccurate expression. According to your advice, we have rewritten it. AAV models for Mir802 knockdown (Figure 3) and Traf3 overexpression (Figure 5) have changed to KD and OE respectively.

6) The statement, "Mir802 expression was unaffected in other organs (Figure S3O)," should clarify that this is except for BAT.

We appreciate the you for this insightful comment. We have clarified that Mir802 expression was unaffected in other organs except for BAT (Figure S3T, revised manuscript).

By addressing these points, the manuscript would present a more robust and clear demonstration of the role of Mir802 in obesity-associated inflammation and metabolic dysfunction.

Thanks for your positive comments. As suggested, we have modified all point.

Reviewer #2 (Public Review):

Yang et al. investigated the role of Mir802 in the development of adipose tissue (AT) inflammation during obesity. The authors found Mir802 levels are up-regulated in the AT of mouse models of obesity and insulin resistance as well as in the AT of humans. They further demonstrated that Mir802 regulates the intracellular levels of TRAF3 and downstream activation of the NF-kB pathway. Ultimately, controlling AT inflammation by manipulating Mir802 affected whole-body glucose homeostasis, highlighting the role of AT inflammatory status in whole-body metabolism. The study provides solid evidence on the role of adipocyte Mir802 in controlling inflammation and macrophage recruitment. However, how lipid mobilization from adipocytes and how engulfment of lipid droplets by macrophages control inflammatory phenotype in these cells could be better explored. The findings of this study will have a great impact in the field, contributing to the growing body of evidence on how microRNAs control the inflammatory microenvironment of AT and whole-body metabolism in obesity.

Thanks for your positive comments.

Reviewer #3 (Public Review):

Mir802 appears to accumulate before macrophage numbers increase in adipose tissue in both mice and humans. The phenotype of Mir802 overexpression and deletion in vivo is sticking and novel. Deletion of Mir802 in adipose tissue after obesity onset also attenuated Adipose inflammation and improved systemic glucose homeostasis. Understanding how Mir802 affects the crosstalk between macrophage and adipocyte is a major point. For example, does Mir802 change the inflammatory of macrophages as it increases Traf3 expression in adipocytes? This is important because macrophages are the input if inflammatory mediators that will activate the TNFR receptor signaling pathway, potentially Traf3, resulting in impaired insulin stimulated Glut4 translocation and glucose uptake. Also, modulation of Mir802 levels in vivo leads to alterations in adiposity. Here, what is a direct effect of Mir802 and what is a result of simply reduced adiposity? One point that os ket is what triggers Mir802 expression, especially in obesity.

Thanks for your important suggestions. According to your suggestions, we have addressed additional data in the revised manuscript to enhance our conclusion.

eLife assessment

This important study utilizes a comprehensive array of animal and cellular models, alongside various techniques, to elucidate the mechanism by which adipose tissue miR-802 contributes to inflammation and metabolic dysfunction in obesity. The data is solid, with clear, reproducible changes showing low variability among biological replicates and consistency across different models. However, some conclusions should be further substantiated with additional data to enhance the scope and strength of the manuscript.

Reviewer #1 (Public Review):

In this manuscript, Yang et al. conduct a comprehensive investigation to demonstrate the role of adipose tissue miR-802 in obesity-associated inflammation and metabolic dysfunction. Using multiple models and techniques, they propose a mechanism where elevated levels of miR-802 in adipose tissue (both in mouse models and humans) trigger fat accumulation and inflammation, leading to increased adiposity and insulin resistance. They suggest that increased miR-802 levels in adipocytes during obesity result in the downregulation of TRAF3, a negative regulator of canonical and non-canonical NF-κB pathways. This downregulation induces inflammation through the production of cytokines/chemokines that attract and polarize macrophages. Concurrently, the NF-κB pathway induces the lipogenic transcriptional factor SREBP1, which promotes fat accumulation and further recruits pro-inflammatory macrophages. While the proposed model is supported by multiple experiments and consistent data, there are areas where the manuscript could be improved. Some improvements can be addressed in the text, while others require additional controls, experiments, or analyses.

(1) The manuscript should provide measurements of lipid droplet/adipocyte size for all models, both in vitro and in vivo. In vivo studies should also include fat weight measurements. This is crucial to determine whether miR-802, TRAF3, and SREBP1 promote adiposity/fat accumulation across all models.<br /> (2) The rationale for co-culture experiments using WAT SVF is unclear, given that miR-802 is upregulated by obesity in adipocytes, not in the stromal-vascular fraction. These experiments would be more relevant if performed using isolated adipocytes or differentiated WAT SVF.<br /> (3) Figures 1G and 1H lack a control group (time 0 or NCD). Without this control, it is impossible to determine if inflammation precedes miR-802 upregulation.<br /> (4) The statement, "The knockout of miR-802 in adipose tissue did not alter food intake, body weight, glucose level, and adiposity (data not shown)," needs more detail regarding the age and sex of the animals. These data are important and should be reported, perhaps in a supplementary figure.<br /> (5) The terms "KO" (knockout) and "KI" (knock-in) are misleading for AAV models, as they do not modify the genome. "KD" (knockdown) and "OE" (overexpression) are more accurate.<br /> (6) The statement, "miR-802 expression was unaffected in other organs (Figure S3O)," should clarify that this is except for BAT.

By addressing these points, the manuscript would present a more robust and clear demonstration of the role of miR-802 in obesity-associated inflammation and metabolic dysfunction.

Reviewer #2 (Public Review):

Yang et al. investigated the role of miR-802 in the development of adipose tissue (AT) inflammation during obesity. The authors found miR-802 levels are up-regulated in the AT of mouse models of obesity and insulin resistance as well as in the AT of humans. They further demonstrated that miR-802 regulates the intracellular levels of TRAF3 and downstream activation of the NF-kB pathway. Ultimately, controlling AT inflammation by manipulating miR-802 affected whole-body glucose homeostasis, highlighting the role of AT inflammatory status in whole-body metabolism. The study provides solid evidence on the role of adipocyte miR-802 in controlling inflammation and macrophage recruitment. However, how lipid mobilization from adipocytes and how engulfment of lipid droplets by macrophages control inflammatory phenotype in these cells could be better explored. The findings of this study will have a great impact in the field, contributing to the growing body of evidence on how microRNAs control the inflammatory microenvironment of AT and whole-body metabolism in obesity.

Reviewer #3 (Public Review):

MiR-802 appears to accumulate before macrophage numbers increase in adipose tissue in both mice and humans. The phenotype of miR-802 overexpression and deletion in vivo is sticking and novel. Deletion of miR-802 in adipose tissue after obesity onset also attenuated Adipose inflammation and improved systemic glucose homeostasis. Understanding how miR-802 affects the crosstalk between macrophage and adipocyte is a major point. For example, does miR-802 change the inflammatory of macrophages as it increases Traf3 expression in adipocytes? This is important because macrophages are the input if inflammatory mediators that will activate the TNFR receptor signaling pathway, potentially Traf3, resulting in impaired insulin stimulated Glut4 translocation and glucose uptake. Also, modulation of miR-802 levels in vivo leads to alterations in adiposity. Here, what is a direct effect of miR-802 and what is a result of simply reduced adiposity? One point that os ket is what triggers miR-802 expression, especially in obesity.

Author response:

Reviewer #1 (Public Review):

In this paper, Tompary & Davachi present work looking at how memories become integrated over time in the brain, and relating those mechanisms to responses on a priming task as a behavioral measure of memory linkage. They find that remotely but not recently formed memories are behaviorally linked and that this is associated with a change in the neural representation in mPFC. They also find that the same behavioral outcomes are associated with the increased coupling of the posterior hippocampus with category-sensitive parts of the neocortex (LOC) during a post-learning rest period-again only for remotely learned information. There was also correspondence in rest connectivity (posterior hippocampus-LOC) and representational change (mPFC) such that for remote memories specifically, the initial post-learning connectivity enhancement during rest related to longer-term mPFC representational change.

This work has many strengths. The topic of this paper is very interesting, and the data provide a really nice package in terms of providing a mechanistic account of how memories become integrated over a delay. The paper is also exceptionally well-written and a pleasure to read. There are two studies, including one large behavioral study, and the findings replicate in the smaller fMRI sample. I do however have two fairly substantive concerns about the analytic approach, where more data will be required before we can know whether the interpretations are an appropriate reflection of the findings. These and other concerns are described below.

Thank you for the positive comments! We are proud of this work, and we feel that the paper is greatly strengthened by the revisions we made in response to your feedback. Please see below for specific changes that we’ve made.

1) One major concern relates to the lack of a pre-encoding baseline scan prior to recent learning.

a) First, I think it would be helpful if the authors could clarify why there was no pre-learning rest scan dedicated to the recent condition. Was this simply a feasibility consideration, or were there theoretical reasons why this would be less "clean"? Including this information in the paper would be helpful for context. Apologies if I missed this detail in the paper.

This is a great point and something that we struggled with when developing this experiment. We considered several factors when deciding whether to include a pre-learning baseline on day two. First, the day 2 scan session was longer than that of day 1 because it included the recognition priming and explicit memory tasks, and the addition of a baseline scan would have made the length of the session longer than a typical scan session – about 2 hours in the scanner in total – and we were concerned that participant engagement would be difficult to sustain across a longer session. Second, we anticipated that the pre-learning scan would not have been a ‘clean’ measure of baseline processing, but rather would include signal related to post-learning processing of the day 1 sequences, as multi-variate reactivation of learned stimuli have been observed in rest scans collected 24-hours after learning (Schlichting & Preston, 2014). We have added these considerations to the Discussion (page 39, lines 1047-1070).

b) Second, I was hoping the authors could speak to what they think is reflected in the post-encoding "recent" scan. Is it possible that these data could also reflect the processing of the remote memories? I think, though am not positive, that the authors may be alluding to this in the penultimate paragraph of the discussion (p. 33) when noting the LOC-mPFC connectivity findings. Could there be the reinstatement of the old memories due to being back in the same experimental context and so forth? I wonder the extent to which the authors think the data from this scan can be reflected as strictly reflecting recent memories, particularly given it is relative to the pre-encoding baseline from before the remote memories, as well (and therefore in theory could reflect both the remote + recent). (I should also acknowledge that, if it is the case that the authors think there might be some remote memory processing during the recent learning session in general, a pre-learning rest scan might not have been "clean" either, in that it could have reflected some processing of the remote memories-i.e., perhaps a clean pre-learning scan for the recent learning session related to point 1a is simply not possible.)

We propose that theoretically, the post-learning recent scan could indeed reflect mixture of remote and recent sequences. This is one of the drawbacks of splitting encoding into two sessions rather than combining encoding into one session and splitting retrieval into an immediate and delayed session; any rest scans that are collected on Day 2 may have signal that relates to processing of the Day 1 remote sequences, which is why we decided against the pre-learning baseline for Day 2, as you had noted.

You are correct that we alluded to in our original submission when discussing the LOC-mPFC coupling result, and we have taken steps to discuss this more explicitly. In Brief, we find greater LOC-mPFC connectivity only after recent learning relative to the pre-learning baseline, and cortical-cortical connectivity could be indicative of processing memories that already have undergone some consolidation (Takashima et al., 2009; Smith et al., 2010). From another vantage point, the mPFC representation of Day 1 learning may have led to increased connectivity with LOC on Day 2 due to Day 1 learning beginning to resemble consolidated prior knowledge (van Kesteren et al., 2010). While this effect is consistent with prior literature and theory, it's unclear why we would find evidence of processing of the remote memories and not the recent memories. Furthermore, the change in LOC-mPFC connectivity in this scan did not correlate with memory behaviors from either learning session, which could be because signal from this scan reflects a mix of processing of the two different learning sessions. With these ideas in mind, we have fleshed out the discussion of the post-encoding ‘recent’ scan in the Discussion (page 38-39, lines 1039-1044).

c) Third, I am thinking about how both of the above issues might relate to the authors' findings, and would love to see more added to the paper to address this point. Specifically, I assume there are fluctuations in baseline connectivity profile across days within a person, such that the pre-learning connectivity on day 1 might be different from on day 2. Given that, and the lack of a pre-learning connectivity measure on day 2, it would logically follow that the measure of connectivity change from pre- to post-learning is going to be cleaner for the remote memories. In other words, could the lack of connectivity change observed for the recent scan simply be due to the lack of a within-day baseline? Given that otherwise, the post-learning rest should be the same in that it is an immediate reflection of how connectivity changes as a function of learning (depending on whether the authors think that the "recent" scan is actually reflecting "recent + remote"), it seems odd that they both don't show the same corresponding increase in connectivity-which makes me think it may be a baseline difference. I am not sure if this is what the authors are implying when they talk about how day 1 is most similar to prior investigation on p. 20, but if so it might be helpful to state that directly.

We agree that it is puzzling that we don’t see that hippocampal-LOC connectivity does not also increase after recent learning, equivalently to what we see after remote learning. However, the fact that there is an increase from baseline rest to post-recent rest in mPFC – LOC connectivity suggests that it’s not an issue with baseline, but rather that the post-recent learning scan is reflecting processing of the remote memories (although as a caveat, there is no relationship with priming).

On what is now page 23, we were referring to the notion that the Day 1 procedure (baseline rest, learning, post-learning rest) is the most straightforward replication of past work that finds a relationship between hippocampal-cortical coupling and later memory. In contrast, the Day 2 learning and rest scan are less ‘clean’ of a replication in that they are taking place in the shadow of Day 1 learning. We have clarified this in the Results (page 23, lines 597-598).

d) Fourth and very related to my point 1c, I wonder if the lack of correlations for the recent scan with behavior is interpretable, or if it might just be that this is a noisy measure due to imperfect baseline correction. Do the authors have any data or logic they might be able to provide that could speak to these points? One thing that comes to mind is seeing whether the raw post-learning connectivity values (separately for both recent and remote) show the same pattern as the different scores. However, the authors may come up with other clever ways to address this point. If not, it might be worth acknowledging this interpretive challenge in the Discussion.

We thought of three different approaches that could help us to understand whether the lack of correlations in between coupling and behavior in the recent scan was due to noise. First, we correlated recognition priming with raw hippocampal-LOC coupling separately for pre- and post-learning scans, as in Author response image 1:

Author response image 1.

Note that the post-learning chart depicts the relationship between post-remote coupling and remote priming and between post-recent coupling and recent priming (middle). Essentially, post-recent learning coupling did not relate to priming of recently learned sequences (middle; green) while there remains a trend for a relationship between post-remote coupling and priming for remotely learned sequences (middle; blue). However, the significant relationship between coupling and priming that we reported in the paper (right, blue) is driven both by the initial negative relationship that is observed in the pre-learning scan and the positive relationship in the post-remote learning scan. This highlights the importance of using a change score, as there may be spurious initial relationships between connectivity profiles and to-be-learned information that would then mask any learning- and consolidation-related changes.

We also reasoned that if comparisons between the post-recent learning scan and the baseline scan are noisier than between the post-remote learning and baseline scan, there may be differences in the variance of the change scores across participants, such that changes in coupling from baseline to post-recent rest may be more variable than coupling from baseline to post-remote rest. We conducted F-tests to compare the variance of the change in these two hippocampal-LO correlations and found no reliable difference (ratio of difference: F(22, 22) = 0.811, p = .63).

Finally, we explored whether hippocampal-LOC coupling is more stable across participants if compared across two rest scans within the same imaging session (baseline and post-remote) versus across two scans across two separate sessions (baseline and post-recent). Interestingly, coupling was not reliably correlated across scans in either case (baseline/post-remote: r = 0.03, p = 0.89 Baseline/post-recent: r = 0.07, p = .74).

Finally, we evaluated whether hippocampal-LOC coupling was correlated across different rest scans (see Author response image 2). We reasoned that if such coupling was more correlated across baseline and post-remote scans relative to baseline and post-recent scans, that would indicate a within-session stability of participants’ connectivity profiles. At the same time, less correlation of coupling across baseline and post-recent scans would be an indication of a noisier change measure as the measure would additionally include a change in individuals’ connectivity profile over time. We found that there was no difference in the correlation of hipp-LO coupling is across sessions, and the correlation was not reliably significant for either session (baseline/post-remote: r = 0.03, p = 0.89; baseline/post-recent: r = 0.07, p = .74; difference: Steiger’s t = 0.12, p = 0.9).

Author response image 2.

We have included the raw correlations with priming (page 25, lines 654-661, Supplemental Figure 6) as well as text describing the comparison of variances (page 25, lines 642-653). We did not add the comparison of hippocampal-LOC coupling across scans to the current manuscript, as an evaluation of stability of such coupling in the context of learning and reactivation seems out of scope of the current focus of the experiment, but we find this result to be worthy of follow-up in future work.

In summary, further analysis of our data did not reveal any indication that a comparison of rest connectivity across scan sessions inserted noise into the change score between baseline and post-recent learning scans. However, these analyses cannot fully rule that possibility out, and the current analyses do not provide concrete evidence that the post-recent learning scan comprises signals that are a mixture of processing of recent and remote sequences. We discuss these drawbacks in the Discussion (page 39, lines 1047-1070).

2) My second major concern is how the authors have operationalized integration and differentiation. The pattern similarity analysis uses an overall correspondence between the neural similarity and a predicted model as the main metric. In the predicted model, C items that are indirectly associated are more similar to one another than they are C items that are entirely unrelated. The authors are then looking at a change in correspondence (correlation) between the neural data and that prediction model from pre- to post-learning. However, a change in the degree of correspondence with the predicted matrix could be driven by either the unrelated items becoming less similar or the related ones becoming more similar (or both!). Since the interpretation in the paper focuses on change to indirectly related C items, it would be important to report those values directly. For instance, as evidence of differentiation, it would be important to show that there is a greater decrease in similarity for indirectly associated C items than it is for unrelated C items (or even a smaller increase) from pre to post, or that C items that are indirectly related are less similar than are unrelated C items post but not pre-learning. Performing this analysis would confirm that the pattern of results matches the authors' interpretation. This would also impact the interpretation of the subsequent analyses that involve the neural integration measures (e.g., correlation analyses like those on p. 16, which may or may not be driven by increased similarity among overlapping C pairs). I should add that given the specificity to the remote learning in mPFC versus recent in LOC and anterior hippocampus, it is clearly the case that something interesting is going on. However, I think we need more data to understand fully what that "something" is.

We recognize the importance of understanding whether model fits (and changes to them) are driven by similarity of overlapping pairs or non-overlapping pairs. We have modified all figures that visualize model fits to the neural integration model to separately show fits for pre- and post-learning (Figure 3 for mPFC, Supp. Figure 5 for LOC, Supp. Figure 9 for AB similarity in anterior hippocampus & LOC). We have additionally added supplemental figures to show the complete breakdown of similarity each region in a 2 (pre/post) x 2 (overlapping/non-overlapping sequence) x 2 (recent/remote) chart. We decided against including only these latter charts rather than the model fits since the model fits strike a good balance between information and readability. We have also modified text in various sections to focus on these new results.

In brief, the decrease in model fit for mPFC for the remote sequences was driven primarily by a decrease in similarity for the overlapping C items and not the non-overlapping ones (Supplementary Figure 3, page 18, lines 468-472).

Interestingly, in LOC, all C items grew more similar after learning, regardless of their overlap or learning session, but the increase in model fit for C items in the recent condition was driven by a larger increase in similarity for overlapping pairs relative to non-overlapping ones (Supp. Figure 5, page 21, lines 533-536).

We also visualized AB similarity in the anterior hippocampus and LOC in a similar fashion (Supplementary Figure 9).

We have also edited the Methods sections with updated details of these analyses (page 52, lines 1392-1397). We think that including these results considerably strengthen our claims and we are pleased to have them included.

3) The priming task occurred before the post-learning exposure phase and could have impacted the representations. More consideration of this in the paper would be useful. Most critically, since the priming task involves seeing the related C items back-to-back, it would be important to consider whether this experience could have conceivably impacted the neural integration indices. I believe it never would have been the case that unrelated C items were presented sequentially during the priming task, i.e., that related C items always appeared together in this task. I think again the specificity of the remote condition is key and perhaps the authors can leverage this to support their interpretation. Can the authors consider this possibility in the Discussion?

It's true that only C items from the same sequence were presented back-to-back during the priming task, and that this presentation may interfere with observations from the post-learning exposure scan that followed it. We agree that it is worth considering this caveat and have added language in the Discussion (page 40, lines 1071-1086). When designing the study, we reasoned that it was more important for the behavioral priming task to come before the exposure scans, as all items were shown only once in that task, whereas they were shown 4-5 times in a random order in the post-learning exposure phase. Because of this difference in presentation times, and because behavioral priming findings tend to be very sensitive, we concluded that it was more important to protect the priming task from the exposure scan instead of the reverse.

We reasoned, however, that the additional presentation of the C items in the recognition priming task would not substantially override the sequence learning, as C items were each presented 16 times in their sequence (ABC1 and ABC2 16 times each). Furthermore, as this reviewer suggests, the order of C items during recognition was the same for recent and remote conditions, so the fact that we find a selective change in neural representation for the remote condition and don’t also see that change for the recent condition is additional assurance that the recognition priming order did not substantially impact the representations.

4) For the priming task, based on the Figure 2A caption it seems as though every sequence contributes to both the control and primed conditions, but (I believe) this means that the control transition always happens first (and they are always back-to-back). Is this a concern? If RTs are changing over time (getting faster), it would be helpful to know whether the priming effects hold after controlling for trial numbers. I do not think this is a big issue because if it were, you would not expect to see the specificity of the remotely learned information. However, it would be helpful to know given the order of these conditions has to be fixed in their design.

This is a correct understanding of the trial orders in the recognition priming task. We chose to involve the baseline items in the control condition to boost power – this way, priming of each sequence could be tested, while only presenting each item once in this task, as repetition in the recognition phase would have further facilitated response times and potentially masked any priming effects. We agree that accounting for trial order would be useful here, so we ran a mixed-effects linear model to examine responses times both as a function of trial number and of priming condition (primed/control). While there is indeed a large effect of trial number such that participants got faster over time, the priming effect originally observed in the remote condition still holds at the same time. We now report this analysis in the Results section (page 14, lines 337-349 for Expt 1 and pages 14-15, lines 360-362 for Expt 2).

5) The authors should be cautious about the general conclusion that memories with overlapping temporal regularities become neurally integrated - given their findings in MPFC are more consistent with overall differentiation (though as noted above, I think we need more data on this to know for sure what is going on).

We realize this conclusion was overly simplistic and, in several places, have revised the general conclusions to be more specific about the nuanced similarity findings.

6) It would be worth stating a few more details and perhaps providing additional logic or justification in the main text about the pre- and post-exposure phases were set up and why. How many times each object was presented pre and post, and how the sequencing was determined (were any constraints put in place e.g., such that C1 and C2 did not appear close in time?). What was the cover task (I think this is important to the interpretation & so belongs in the main paper)? Were there considerations involving the fact that this is a different sequence of the same objects the participants would later be learning - e.g., interference, etc.?

These details can be found in the Methods section (pages 50-51, lines 1337-1353) and we’ve added a new summary of that section in the Results (page 17, lines 424- 425 and 432-435). In brief, a visual hash tag appeared on a small subset of images and participants pressed a button when this occurred, and C1 and C2 objects were presented in separate scans (as were A and B objects) to minimize inflated neural similarity due to temporal proximity.

Reviewer #2 (Public Review):

The manuscript by Tompary & Davachi presents results from two experiments, one behavior only and one fMRI plus behavior. They examine the important question of how to separate object memories (C1 and C2) that are never experienced together in time and become linked by shared predictive cues in a sequence (A followed by B followed by one of the C items). The authors developed an implicit priming task that provides a novel behavioral metric for such integration. They find significant C1-C2 priming for sequences that were learned 24h prior to the test, but not for recently learned sequences, suggesting that associative links between the two originally separate memories emerge over an extended period of consolidation. The fMRI study relates this behavioral integration effect to two neural metrics: pattern similarity changes in the medial prefrontal cortex (mPFC) as a measure of neural integration, and changes in hippocampal-LOC connectivity as a measure of post-learning consolidation. While fMRI patterns in mPFC overall show differentiation rather than integration (i.e., C1-C2 representational distances become larger), the authors find a robust correlation such that increasing pattern similarity in mPFC relates to stronger integration in the priming test, and this relationship is again specific to remote memories. Moreover, connectivity between the posterior hippocampus and LOC during post-learning rest is positively related to the behavioral integration effect as well as the mPFC neural similarity index, again specifically for remote memories. Overall, this is a coherent set of findings with interesting theoretical implications for consolidation theories, which will be of broad interest to the memory, learning, and predictive coding communities.

Strengths:

1) The implicit associative priming task designed for this study provides a promising new tool for assessing the formation of mnemonic links that influence behavior without explicit retrieval demands. The authors find an interesting dissociation between this implicit measure of memory integration and more commonly used explicit inference measures: a priming effect on the implicit task only evolved after a 24h consolidation period, while the ability to explicitly link the two critical object memories is present immediately after learning. While speculative at this point, these two measures thus appear to tap into neocortical and hippocampal learning processes, respectively, and this potential dissociation will be of interest to future studies investigating time-dependent integration processes in memory.

2) The experimental task is well designed for isolating pre- vs post-learning changes in neural similarity and connectivity, including important controls of baseline neural similarity and connectivity.

3) The main claim of a consolidation-dependent effect is supported by a coherent set of findings that relate behavioral integration to neural changes. The specificity of the effects on remote memories makes the results particularly interesting and compelling.

4) The authors are transparent about unexpected results, for example, the finding that overall similarity in mPFC is consistent with a differentiation rather than an integration model.

Thank you for the positive comments!

Weaknesses:

1) The sequence learning and recognition priming tasks are cleverly designed to isolate the effects of interest while controlling for potential order effects. However, due to the complex nature of the task, it is difficult for the reader to infer all the transition probabilities between item types and how they may influence the behavioral priming results. For example, baseline items (BL) are interspersed between repeated sequences during learning, and thus presumably can only occur before an A item or after a C item. This seems to create non-random predictive relationships such that C is often followed by BL, and BL by A items. If this relationship is reversed during the recognition priming task, where the sequence is always BL-C1-C2, this violation of expectations might slow down reaction times and deflate the baseline measure. It would be helpful if the manuscript explicitly reported transition probabilities for each relevant item type in the priming task relative to the sequence learning task and discussed how a match vs mismatch may influence the observed priming effects.

We have added a table of transition probabilities across the learning, recognition priming, and exposure scans (now Table 1, page 48). We have also included some additional description of the change in transition probabilities across different tasks in the Methods section. Specifically, if participants are indeed learning item types and rules about their order, then both the control and the primed conditions would violate that order. Since C1 and C2 items never appeared together, viewing C1 would give rise to an expectation of seeing a BL item, which would also be violated. This suggests that our priming effects are driven by sequence-specific relationships rather than learning of the probabilities of different item types. We’ve added this consideration to the Methods section (page 45, lines 1212-1221).

Another critical point to consider (and that the transition probabilities do not reflect) is that during learning, while C is followed either by A or BL, they are followed by different A or BL items. In contrast, a given A is always followed by the same B object, which is always followed by one of two C objects. While the order of item types is semi-predictable, the order of objects (specific items) themselves are not. This can be seen in the response times during learning, such that response times for A and BL items are always slower than for B and C items. We have explained this nuance in the figure text for Table 1.

2) The choice of what regions of interest to include in the different sets of analyses could be better motivated. For example, even though briefly discussed in the intro, it remains unclear why the posterior but not the anterior hippocampus is of interest for the connectivity analyses, and why the main target is LOC, not mPFC, given past results including from this group (Tompary & Davachi, 2017). Moreover, for readers not familiar with this literature, it would help if references were provided to suggest that a predictable > unpredictable contrast is well suited for functionally defining mPFC, as done in the present study.

We have clarified our reasoning for each of these choices throughout the manuscript and believe that our logic is now much more transparent. For an expanded reasoning of why we were motivated to look at posterior and not anterior hippocampus, see pages 6-7, lines 135-159, and our response to R2. In brief, past research focusing on post-encoding connectivity with the hippocampus suggests that posterior aspect is more likely to couple with category-selective cortex after learning neutral, non-rewarded objects much like the stimuli used in the present study.

We also clarify our reasoning for LOC over mPFC. While theoretically, mPFC is thought to be a candidate region for coupling with the hippocampus during consolidation, the bulk of empirical work to date has revealed post-encoding connectivity between the hippocampus and category-selective cortex in the ventral and occipital lobes (page 6, lines 123-134).

As for the use of the predictable > unpredictable contrast for functionally defining cortical regions, we reasoned that cortical regions that were sensitive to the temporal regularities generated by the sequences may be further involved in their offline consolidation and long-term storage (Danker & Anderson, 2010; Davachi & Danker, 2013; McClelland et al., 1995). We have added this justification to the Methods section (page 18, lines 454-460).

3) Relatedly, multiple comparison corrections should be applied in the fMRI integration and connectivity analyses whenever the same contrast is performed on multiple regions in an exploratory manner.

We now correct for multiple comparisons using Bonferroni correction, and this correction depends on the number of regions in which each analysis is conducted. Please see page 55, lines 1483-1490, in the Methods section for details of each analysis.

Reviewer #3 (Public Review):

The authors of this manuscript sought to illuminate a link between a behavioral measure of integration and neural markers of cortical integration associated with systems consolidation (post-encoding connectivity, change in representational neural overlap). To that aim, participants incidentally encoded sequences of objects in the fMRI scanner. Unbeknownst to participants, the first two objects of the presented ABC triplet sequences overlapped for a given pair of sequences. This allowed the authors to probe the integration of unique C objects that were never directly presented in the same sequence, but which shared the same preceding A and B objects. They encoded one set of objects on Day 1 (remote condition), another set of objects 24 hours later (recent condition) and tested implicit and explicit memory for the learned sequences on Day 2. They additionally collected baseline and post-encoding resting-state scans. As their measure of behavioral integration, the authors examined reaction time during an Old/New judgement task for C objects depending on if they were preceded by a C object from an overlapping sequence (primed condition) versus a baseline object. They found faster reaction times for the primed objects compared to the control condition for remote but not recently learned objects, suggesting that the C objects from overlapping sequences became integrated over time. They then examined pattern similarity in a priori ROIs as a measure of neural integration and found that participants showing evidence of integration of C objects from overlapping sequences in the medial prefrontal cortex for remotely learned objects also showed a stronger implicit priming effect between those C objects over time. When they examined the change in connectivity between their ROIs after encoding, they also found that connectivity between the posterior hippocampus and lateral occipital cortex correlated with larger priming effects for remotely learned objects, and that lateral occipital connectivity with the medial prefrontal cortex was related to neural integration of remote objects from overlapping sequences.

The authors aim to provide evidence of a relationship between behavioral and neural measures of integration with consolidation is interesting, important, and difficult to achieve given the longitudinal nature of studies required to answer this question. Strengths of this study include a creative behavioral task, and solid modelling approaches for fMRI data with careful control for several known confounds such as bold activation on pattern analysis results, motion, and physiological noise. The authors replicate their behavioral observations across two separate experiments, one of which included a large sample size, and found similar results that speak to the reliability of the observed behavioral phenomenon. In addition, they document several correlations between neural measures and task performance, lending functional significance to their neural findings.

Thank you for this positive assessment of our study!

However, this study is not without notable weaknesses that limit the strength of the manuscript. The authors report a behavioral priming effect suggestive of integration of remote but not recent memories, leading to the interpretation that the priming effect emerges with consolidation. However, they did not observe a reliable interaction between the priming condition and learning session (recent/remote) on reaction times, meaning that the priming effect for remote memories was not reliably greater than that observed for recent. In addition, the emergence of a priming effect for remote memories does not appear to be due to faster reaction times for primed targets over time (the condition of interest), but rather, slower reaction times for control items in the remote condition compared to recent. These issues limit the strength of the claim that the priming effect observed is due to C items of interest being integrated in a consolidation-dependent manner.

We acknowledge that the lack of a day by condition interaction in the behavioral priming effect should discussed and now discuss this data in a more nuanced manner. While it’s true that the priming effect emerges due to a slowing of the control items over time, this slowing is consistent with classic time-dependent effects demonstrating slower response times for more delayed memories. The fact that the response times in the primed condition does not show this slowing can be interpreted as a protection against this slowing that would otherwise occur. Please see page 29, lines 758-766, for this added discussion.

Similarly, the interactions between neural variables of interest and learning session needed to strongly show a significant consolidation-related effect in the brain were sometimes tenuous. There was no reliable difference in neural representational pattern analysis fit to a model of neural integration between the short and long delays in the medial prefrontal cortex or lateral occipital cortex, nor was the posterior hippocampus-lateral occipital cortex post-encoding connectivity correlation with subsequent priming significantly different for recent and remote memories. While the relationship between integration model fit in the medial prefrontal cortex and subsequent priming (which was significantly different from that occurring for recent memories) was one of the stronger findings of the paper in favor of a consolidation-related effect on behavior, is it possible that lack of a behavioral priming effect for recent memories due to possible issues with the control condition could mask a correlation between neural and behavioral integration in the recent memory condition?

While we acknowledge that lack of a statistically reliable interaction between neural measures and behavioral priming in many cases, we are heartened by the reliable difference in the relationship between mPFC similarity and priming over time, which was our main planned prediction. In addition to adding caveats in the discussion about the neural measures and behavioral findings in the recent condition (see our response to R1.1 and R1.4 for more details), we have added language throughout the manuscript noting the need to interpret these data with caution.

These limitations are especially notable when one considers that priming does not classically require a period of prolonged consolidation to occur, and prominent models of systems consolidation rather pertain to explicit memory. While the authors have provided evidence that neural integration in the medial prefrontal cortex, as well as post-encoding coupling between the lateral occipital cortex and posterior hippocampus, are related to faster reaction times for primed objects of overlapping sequences compared to their control condition, more work is needed to verify that the observed findings indeed reflect consolidation dependent integration as proposed.

We agree that more work is needed to provide converging evidence for these novel findings. However, we wish to counter the notion that systems consolidation models are relevant only for explicit memories. Although models of systems consolidation often mention transformations from episodic to semantic memory, the critical mechanisms that define the models involve changes in the neural ensembles of a memory that is initially laid down in the hippocampus and is taught to cortex over time. This transformation of neural traces is not specific to explicit/declarative forms of memory. For example, implicit statistical learning initially depends on intact hippocampal function (Schapiro et al., 2014) and improves over consolidation (Durrant et al., 2011, 2013; Kóbor et al., 2017).

Second, while there are many classical findings of priming during or immediately after learning, there are several instances of priming used to measure consolidation-related changes to newly learned information. For instance, priming has been used as a measure of lexical integration, demonstrating that new word learning benefits from a night of sleep (Wang et al., 2017; Gaskell et al., 2019) or a 1-week delay (Tamminen & Gaskell, 2013). The issue is not whether priming can occur immediately, it is whether priming increases with a delay.

Finally, it is helpful to think about models of memory systems that divide memory representations not by their explicit/implicit nature, but along other important dimensions such as their neural bases, their flexibility vs rigidity, and their capacity for rapid vs slow learning (Henke, 2010). Considering this evidence, we suggest that systems consolidation models are most useful when considering how transformations in the underlying neural memory representation affects its behavioral expression, rather than focusing on the extent that the memory representation is explicit or implicit.

With all this said, we have added text to the discussion reminding the reader that there was no statistically significant difference in priming as a function of the delay (page 29, lines 764 - 766). However, we are encouraged by the fact that the relationship between priming and mPFC neural similarity was significantly stronger for remotely learned objects relative to recently learned ones, as this is directly in line with systems consolidation theories.

References

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eLife assessment

This important study investigates how memory representations are transformed over time (24h period). The work advances our understanding of the neural processes supporting the behavioral integration of memories for distinct events that are never experienced together in time but are linked by shared predictive cues. Evidence supporting the claims is solid, and reporting of additional comparisons would have strengthened the study.

Reviewer #1 (Public Review):

In this paper, Tompary & Davachi present work looking at how memories become integrated over time in the brain, and relating those mechanisms to responses on a priming task as a behavioral measure of memory linkage. They find that remotely but not recently formed memories are behaviorally linked and that this is associated with a change in the neural representation in mPFC. They also find that the same behavioral outcomes are associated with the increased coupling of the posterior hippocampus with category-sensitive parts of the neocortex (LOC) during a post-learning rest period-again only for remotely learned information. There was also correspondence in rest connectivity (posterior hippocampus-LOC) and representational change (mPFC) such that for remote memories specifically, the initial post-learning connectivity enhancement during rest related to longer-term mPFC representational change.

This work has many strengths. The topic of this paper is very interesting, and the data provide a really nice package in terms of providing a mechanistic account of how memories become integrated over a delay. The paper is also exceptionally well-written and a pleasure to read. There are two studies, including one large behavioral study, and the findings replicate in the smaller fMRI sample. I do however have two fairly substantive concerns about the analytic approach, where more data will be required before we can know whether the interpretations are an appropriate reflection of the findings. These and other concerns are described below.

(1) One major concern relates to the lack of a pre-encoding baseline scan prior to recent learning.

a) First, I think it would be helpful if the authors could clarify why there was no pre-learning rest scan dedicated to the recent condition. Was this simply a feasibility consideration, or were there theoretical reasons why this would be less "clean"? Including this information in the paper would be helpful for context. Apologies if I missed this detail in the paper.

b) Second, I was hoping the authors could speak to what they think is reflected in the post-encoding "recent" scan. Is it possible that these data could also reflect the processing of the remote memories? I think, though am not positive, that the authors may be alluding to this in the penultimate paragraph of the discussion (p. 33) when noting the LOC-mPFC connectivity findings. Could there be the reinstatement of the old memories due to being back in the same experimental context and so forth? I wonder the extent to which the authors think the data from this scan can be reflected as strictly reflecting recent memories, particularly given it is relative to the pre-encoding baseline from before the remote memories, as well (and therefore in theory could reflect both the remote + recent). (I should also acknowledge that, if it is the case that the authors think there might be some remote memory processing during the recent learning session in general, a pre-learning rest scan might not have been "clean" either, in that it could have reflected some processing of the remote memories-i.e., perhaps a clean pre-learning scan for the recent learning session related to point 1a is simply not possible.)

c) Third, I am thinking about how both of the above issues might relate to the authors' findings, and would love to see more added to the paper to address this point. Specifically, I assume there are fluctuations in baseline connectivity profile across days within a person, such that the pre-learning connectivity on day 1 might be different from on day 2. Given that, and the lack of a pre-learning connectivity measure on day 2, it would logically follow that the measure of connectivity change from pre- to post-learning is going to be cleaner for the remote memories. In other words, could the lack of connectivity change observed for the recent scan simply be due to the lack of a within-day baseline? Given that otherwise, the post-learning rest should be the same in that it is an immediate reflection of how connectivity changes as a function of learning (depending on whether the authors think that the "recent" scan is actually reflecting "recent + remote"), it seems odd that they both don't show the same corresponding increase in connectivity-which makes me think it may be a baseline difference. I am not sure if this is what the authors are implying when they talk about how day 1 is most similar to prior investigation on p. 20, but if so it might be helpful to state that directly.

d) Fourth and very related to my point 1c, I wonder if the lack of correlations for the recent scan with behavior is interpretable, or if it might just be that this is a noisy measure due to imperfect baseline correction. Do the authors have any data or logic they might be able to provide that could speak to these points? One thing that comes to mind is seeing whether the raw post-learning connectivity values (separately for both recent and remote) show the same pattern as the different scores. However, the authors may come up with other clever ways to address this point. If not, it might be worth acknowledging this interpretive challenge in the Discussion.

(2) My second major concern is how the authors have operationalized integration and differentiation. The pattern similarity analysis uses an overall correspondence between the neural similarity and a predicted model as the main metric. In the predicted model, C items that are indirectly associated are more similar to one another than they are C items that are entirely unrelated. The authors are then looking at a change in correspondence (correlation) between the neural data and that prediction model from pre- to post-learning. However, a change in the degree of correspondence with the predicted matrix could be driven by either the unrelated items becoming less similar or the related ones becoming more similar (or both!). Since the interpretation in the paper focuses on change to indirectly related C items, it would be important to report those values directly. For instance, as evidence of differentiation, it would be important to show that there is a greater decrease in similarity for indirectly associated C items than it is for unrelated C items (or even a smaller increase) from pre to post, or that C items that are indirectly related are less similar than are unrelated C items post but not pre-learning. Performing this analysis would confirm that the pattern of results matches the authors' interpretation. This would also impact the interpretation of the subsequent analyses that involve the neural integration measures (e.g., correlation analyses like those on p. 16, which may or may not be driven by increased similarity among overlapping C pairs). I should add that given the specificity to the remote learning in mPFC versus recent in LOC and anterior hippocampus, it is clearly the case that something interesting is going on. However, I think we need more data to understand fully what that "something" is.

(3) The priming task occurred before the post-learning exposure phase and could have impacted the representations. More consideration of this in the paper would be useful. Most critically, since the priming task involves seeing the related C items back-to-back, it would be important to consider whether this experience could have conceivably impacted the neural integration indices. I believe it never would have been the case that unrelated C items were presented sequentially during the priming task, i.e., that related C items always appeared together in this task. I think again the specificity of the remote condition is key and perhaps the authors can leverage this to support their interpretation. Can the authors consider this possibility in the Discussion?

(4) For the priming task, based on the Figure 2A caption it seems as though every sequence contributes to both the control and primed conditions, but (I believe) this means that the control transition always happens first (and they are always back-to-back). Is this a concern? If RTs are changing over time (getting faster), it would be helpful to know whether the priming effects hold after controlling for trial numbers. I do not think this is a big issue because if it were, you would not expect to see the specificity of the remotely learned information. However, it would be helpful to know given the order of these conditions has to be fixed in their design.

(5) The authors should be cautious about the general conclusion that memories with overlapping temporal regularities become neurally integrated - given their findings in MPFC are more consistent with overall differentiation (though as noted above, I think we need more data on this to know for sure what is going on).

(6) It would be worth stating a few more details and perhaps providing additional logic or justification in the main text about the pre and post-exposure phases were set up and why. How many times each object was presented pre and post, and how the sequencing was determined (were any constraints put in place e.g., such that C1 and C2 did not appear close in time?). What was the cover task (I think this is important to the interpretation & so belongs in the main paper)? Were there considerations involving the fact that this is a different sequence of the same objects the participants would later be learning - e.g., interference, etc.?

Reviewer #2 (Public Review):

The manuscript by Tompary & Davachi presents results from two experiments, one behavior only and one fMRI plus behavior. They examine the important question of how to separate object memories (C1 and C2) that are never experienced together in time and become linked by shared predictive cues in a sequence (A followed by B followed by one of the C items). The authors developed an implicit priming task that provides a novel behavioral metric for such integration. They find significant C1-C2 priming for sequences that were learned 24h prior to the test, but not for recently learned sequences, suggesting that associative links between the two originally separate memories emerge over an extended period of consolidation. The fMRI study relates this behavioral integration effect to two neural metrics: pattern similarity changes in the medial prefrontal cortex (mPFC) as a measure of neural integration, and changes in hippocampal-LOC connectivity as a measure of post-learning consolidation. While fMRI patterns in mPFC overall show differentiation rather than integration (i.e., C1-C2 representational distances become larger), the authors find a robust correlation such that increasing pattern similarity in mPFC relates to stronger integration in the priming test, and this relationship is again specific to remote memories. Moreover, connectivity between the posterior hippocampus and LOC during post-learning rest is positively related to the behavioral integration effect as well as the mPFC neural similarity index, again specifically for remote memories. Overall, this is a coherent set of findings with interesting theoretical implications for consolidation theories, which will be of broad interest to the memory, learning, and predictive coding communities.

Strengths:

(1) The implicit associative priming task designed for this study provides a promising new tool for assessing the formation of mnemonic links that influence behavior without explicit retrieval demands. The authors find an interesting dissociation between this implicit measure of memory integration and more commonly used explicit inference measures: a priming effect on the implicit task only evolved after a 24h consolidation period, while the ability to explicitly link the two critical object memories is present immediately after learning. While speculative at this point, these two measures thus appear to tap into neocortical and hippocampal learning processes, respectively, and this potential dissociation will be of interest to future studies investigating time-dependent integration processes in memory.

(2) The experimental task is well designed for isolating pre- vs post-learning changes in neural similarity and connectivity, including important controls of baseline neural similarity and connectivity.

(3) The main claim of a consolidation-dependent effect is supported by a coherent set of findings that relate behavioral integration to neural changes. The specificity of the effects on remote memories makes the results particularly interesting and compelling.

(4) The authors are transparent about unexpected results, for example, the finding that overall similarity in mPFC is consistent with a differentiation rather than an integration model.

Weaknesses:

(1) The sequence learning and recognition priming tasks are cleverly designed to isolate the effects of interest while controlling for potential order effects. However, due to the complex nature of the task, it is difficult for the reader to infer all the transition probabilities between item types and how they may influence the behavioral priming results. For example, baseline items (BL) are interspersed between repeated sequences during learning, and thus presumably can only occur before an A item or after a C item. This seems to create non-random predictive relationships such that C is often followed by BL, and BL by A items. If this relationship is reversed during the recognition priming task, where the sequence is always BL-C1-C2, this violation of expectations might slow down reaction times and deflate the baseline measure. It would be helpful if the manuscript explicitly reported transition probabilities for each relevant item type in the priming task relative to the sequence learning task and discussed how a match vs mismatch may influence the observed priming effects.

(2) The choice of what regions of interest to include in the different sets of analyses could be better motivated. For example, even though briefly discussed in the intro, it remains unclear why the posterior but not the anterior hippocampus is of interest for the connectivity analyses, and why the main target is LOC, not mPFC, given past results including from this group (Tompary & Davachi, 2017). Moreover, for readers not familiar with this literature, it would help if references were provided to suggest that a predictable > unpredictable contrast is well suited for functionally defining mPFC, as done in the present study.

(3) Relatedly, multiple comparison corrections should be applied in the fMRI integration and connectivity analyses whenever the same contrast is performed on multiple regions in an exploratory manner.

Reviewer #3 (Public Review):

The authors of this manuscript sought to illuminate a link between a behavioral measure of integration and neural markers of cortical integration associated with systems consolidation (post-encoding connectivity, change in representational neural overlap). To that aim, participants incidentally encoded sequences of objects in the fMRI scanner. Unbeknownst to participants, the first two objects of the presented ABC triplet sequences overlapped for a given pair of sequences. This allowed the authors to probe the integration of unique C objects that were never directly presented in the same sequence, but which shared the same preceding A and B objects. They encoded one set of objects on Day 1 (remote condition), another set of objects 24 hours later (recent condition) and tested implicit and explicit memory for the learned sequences on Day 2. They additionally collected baseline and post-encoding resting-state scans. As their measure of behavioral integration, the authors examined reaction time during an Old/New judgement task for C objects depending on if they were preceded by a C object from an overlapping sequence (primed condition) versus a baseline object. They found faster reaction times for the primed objects compared to the control condition for remote but not recently learned objects, suggesting that the C objects from overlapping sequences became integrated over time. They then examined pattern similarity in a priori ROIs as a measure of neural integration and found that participants showing evidence of integration of C objects from overlapping sequences in the medial prefrontal cortex for remotely learned objects also showed a stronger implicit priming effect between those C objects over time. When they examined the change in connectivity between their ROIs after encoding, they also found that connectivity between the posterior hippocampus and lateral occipital cortex correlated with larger priming effects for remotely learned objects, and that lateral occipital connectivity with the medial prefrontal cortex was related to neural integration of remote objects from overlapping sequences.

The authors aim to provide evidence of a relationship between behavioral and neural measures of integration with consolidation is interesting, important, and difficult to achieve given the longitudinal nature of studies required to answer this question. Strengths of this study include a creative behavioral task, and solid modelling approaches for fMRI data with careful control for several known confounds such as bold activation on pattern analysis results, motion, and physiological noise. The authors replicate their behavioral observations across two separate experiments, one of which included a large sample size, and found similar results that speak to the reliability of the observed behavioral phenomenon. In addition, they document several correlations between neural measures and task performance, lending functional significance to their neural findings.

However, this study is not without notable weaknesses that limit the strength of the manuscript. The authors report a behavioral priming effect suggestive of integration of remote but not recent memories, leading to the interpretation that the priming effect emerges with consolidation. However, they did not observe a reliable interaction between the priming condition and learning session (recent/remote) on reaction times, meaning that the priming effect for remote memories was not reliably greater than that observed for recent. In addition, the emergence of a priming effect for remote memories does not appear to be due to faster reaction times for primed targets over time (the condition of interest), but rather, slower reaction times for control items in the remote condition compared to recent. These issues limit the strength of the claim that the priming effect observed is due to C items of interest being integrated in a consolidation-dependent manner.

Similarly, the interactions between neural variables of interest and learning session needed to strongly show a significant consolidation-related effect in the brain were sometimes tenuous. There was no reliable difference in neural representational pattern analysis fit to a model of neural integration between the short and long delays in the medial prefrontal cortex or lateral occipital cortex, nor was the posterior hippocampus-lateral occipital cortex post-encoding connectivity correlation with subsequent priming significantly different for recent and remote memories. While the relationship between integration model fit in the medial prefrontal cortex and subsequent priming (which was significantly different from that occurring for recent memories) was one of the stronger findings of the paper in favor of a consolidation-related effect on behavior, is it possible that lack of a behavioral priming effect for recent memories due to possible issues with the control condition could mask a correlation between neural and behavioral integration in the recent memory condition?

These limitations are especially notable when one considers that priming does not classically require a period of prolonged consolidation to occur, and prominent models of systems consolidation rather pertain to explicit memory. While the authors have provided evidence that neural integration in the medial prefrontal cortex, as well as post-encoding coupling between the lateral occipital cortex and posterior hippocampus, are related to faster reaction times for primed objects of overlapping sequences compared to their control condition, more work is needed to verify that the observed findings indeed reflect consolidation dependent integration as proposed.

eLife assessment

This important computational study provides new insights into how neural dynamics may lead to time-evolving behavioral errors as observed in certain working-memory tasks. By combining ideas from efficient coding and attractor neural networks, the authors construct a two-module network model to capture the sensory-memory interactions and the distributed nature of working memory representations. They provide convincing evidence supporting that their two-module network, but not any of the alternative circuit structures they considered, can account for error patterns reported in orientation estimation tasks with delays.

Reviewer #1 (Public Review):

Summary:

Working memory is imperfect - memories accrue error over time and are biased towards certain identities. For example, previous work has shown memory for orientation is more accurate near the cardinal directions (i.e., variance in responses is smaller for horizontal and vertical stimuli) while being biased towards diagonal orientations (i.e., there is a repulsive bias away from horizontal and vertical stimuli). The magnitude of errors and biases increase the longer an item is held in working memory and when more items are held in working memory (i.e., working memory load is higher). Previous work has argued that biases and errors could be explained by increased perceptual acuity at cardinal directions. However, these models are constrained to sensory perception and do not explain how biases and errors increase over time in memory. The current manuscript builds on this work to show how a two-layer neural network could integrate errors and biases over a memory delay. In brief, the model includes a 'sensory' layer with heterogenous connections that lead to the repulsive bias and decreased error at the cardinal directions. This layer is then reciprocally connected with a classic ring attractor layer. Through their reciprocal interactions, the biases in the sensory layer are constantly integrated into the representation in memory. In this way, the model captures the distribution of biases and errors for different orientations that has been seen in behavior and their increasing magnitude with time. The authors compare the two-layer network to a simpler one-network model, showing that the one model network is harder to tune and shows an attractive bias for memories that have lower error (which is incompatible with empirical results).

Strengths:

The manuscript provides a nice review of the dynamics of items in working memory, showing how errors and biases differ across stimulus space. The two-layer neural network model is able to capture the behavioral effects as well as relate to neurophysiological observations that memory representations are distributed across sensory cortex and prefrontal cortex.

The authors use multiple approaches to understand how the network produces the observed results. For example, analyzing the dynamics of memories in the low-dimensional representational space of the networks provides the reader with an intuition for the observed effects.

As a point of comparison with the two-layer network, the authors construct a heterogenous one-layer network (analogous to a single memory network with embedded biases). They argue that such a network is incapable of capturing the observed behavioral effects but could potentially explain biases and noise levels in other sensory domains where attractive biases have lower errors (e.g., color).

The authors show how changes in the strength of Hebbian learning of excitatory and inhibitory synapses can change network behavior. This argues for relatively stronger learning in inhibitory synapses, an interesting prediction.

The manuscript is well-written. In particular, the figures are well done and nicely schematize the model and the results.

Weaknesses:

Despite its strengths, the manuscript does have some weaknesses. These weaknesses are adequately discussed in the manuscript and motivate future research.

One weakness is that the model is not directly fit to behavioral data, but rather compared to a schematic of behavioral data. As noted above, the model provides insight into the general phenomenon of biases in working memory. However, because the models are not fit directly to data, they may miss some aspects of the data.

In addition, directly fitting the models to behavioral data could allow for a broader exploration of parameter space for both the one-layer and two-layer models (and their alternatives). Such an approach would provide stronger support for the papers claims (such as "....these evolving errors...require network interaction between two distinct modules."). That being said, the manuscript does explore several alternative models and also acknowledges the limitation of not directly fitting behavior, due to difficulties in fitting complex neural network models to data.

One important behavioral observation is that both diffusive noise and biases increase with the number of items in working memory. The current model does not capture these effects and it isn't clear how the model architecture could be extended to capture these effects. That being said, the authors note this limitation in the Discussion and present it as a future direction.

Overall:

Overall, the manuscript was successful in building a model that captured the biases and noise observed in working memory. This work complements previous studies that have viewed these effects through the lens of optimal coding, extending these models to explain the effects of time in memory. In addition, the two-layer network architecture extends previous work with similar architectures, adding further support to the distributed nature of working memory representations.

Reviewer #2 (Public Review):

In this manuscript, Yang et al. present a modeling framework to understand the pattern of response biases and variance observed in delayed-response orientation estimation tasks. They combine a series of modeling approaches to show that coupled sensory-memory networks are in a better position than single-area models to support experimentally observed delay-dependent response bias and variance in cardinal compared to oblique orientations. These errors can emerge from a population-code approach that implements efficient coding and Bayesian inference principles and is coupled to a memory module that introduces random maintenance errors. A biological implementation of such operation is found when coupling two neural network modules, a sensory module with connectivity inhomogeneities that reflect environment priors, and a memory module with strong homogeneous connectivity that sustains continuous ring attractor function. Comparison with single-network solutions that combine both connectivity inhomogeneities and memory attractors shows that two-area models can more easily reproduce the patterns of errors observed experimentally.

Strengths:

The model provides an integration of two modeling approaches to the computational bases of behavioral biases: one based on Bayesian and efficient coding principles, and one based on attractor dynamics. These two perspectives are not usually integrated consistently in existing studies, which this manuscript beautifully achieves. This is a conceptual advancement, especially because it brings together the perceptual and memory components of common laboratory tasks.

The proposed two-area model provides a biologically plausible implementation of efficient coding and Bayesian inference principles, which interact seamlessly with a memory buffer to produce a complex pattern of delay-dependent response errors. No previous model had achieved this.

Weaknesses:

The correspondence between the various computational models is not clearly shown. It is not easy to see clearly this correspondence because network function is illustrated with different representations for different models. In particular, the Bayesian model of Figure 2 is illustrated with population responses for different stimuli and delays, while the attractor models of Figure 3 and 4 are illustrated with neuronal tuning curves but not population activity.

The proposed model has stronger feedback than feedforward connections between the sensory and memory modules (J_f = 0.1 and J_b = 0.25). This is not the common assumption when thinking about hierarchical processing in the brain. The manuscript argues that error patterns remain similar as long as the product of J_f and J_b is constant, so it is unclear why the authors preferred this network example as opposed to one with J_b = 0.1 and J_f = 0.25.

Reviewer #3 (Public Review):

Summary:

The present study proposes a neural circuit model consisting of coupled sensory and memory networks to explain the circuit mechanism of the cardinal effect in orientation perception which is characterized by the bias towards the oblique orientation and the largest variance at the oblique orientation.

Strengths:

The authors have done numerical simulations and preliminary analysis of the neural circuit model to show the model successfully reproduces the cardinal effect. And the paper is well-written overall. As far as I know, most of the studies on the cardinal effect are at the level of statistical models, and the current study provides one possibility of how neural circuit models reproduce such an effect.

Weaknesses:

There are no major weaknesses and flaws in the present study, although I suggest the author conduct further analysis to deepen our understanding of the circuit mechanism of the cardinal effects. Please find my recommendations for concrete comments.

Author response:

The following is the authors’ response to the original reviews.

In this important paper, the authors propose a computational model for understanding how the dynamics of neural representations may lead to specific patterns of errors as observed in working memory tasks. The paper provides solid evidence showing how a two-area model of sensory-memory interactions can account for the error patterns reported in orientation estimation tasks with delays. By integrating ideas from efficient coding and attractor networks, the resulting theoretical framework is appealing, and nicely captures some basic patterns of behavior data and the distributed nature of memory representation as reported in prior neurophysiological studies. The paper can be strengthened if (i) further analyses are conducted to deepen our understanding of the circuit mechanisms underlying the behavior effects; (ii) the necessity of the two-area network model is better justified; (iii) the nuanced aspects of the behavior that are not captured by the current model are discussed in more detail.

We thank the Editors and Reviewers for their constructive comments. In response to the suggestions provided, we have implemented the following revisions:

- Clarified the origin of the specific pattern of diffusion: We showed that variance patterns remain consistent across different noise types or levels in new Figure 5 – Figure supplement 2 and Figure 9 – Figure supplement 1 (uniform Gaussian noise with varying strengths). This is connected to the representation geometry induced by heterogeneous connections (Eq. 21).

- Provided an intuitive explanation of the two-module network’s advantages: Additional simulations demonstrated that heterogeneity degree of sensory connections and intermodal connection strengths affect drift and diffusion terms differently (new Figure 6). This endows an extra degree of freedom in controlling heterogeneity in drift and diffusion terms in the two-module network (new Figure 9).

- Addressed a limitation and future directions in the Discussion: Our study is limited to the dynamic evolution of memory representation for a single orientation stimulus and its associated error patterns. We acknowledge the need for further investigation to capture nuanced error patterns in broader experimental settings, such as changes in error patterns for varying stimulus presentation durations in perception tasks. We have discussed potential extensions, such as incorporating more biologically plausible baseline activities, external noise, or variations of loss functions.

Additionally, we showed consistent error patterns when decoded from activities of the sensory module (Figure 4 – Figure supplement 1), and incorrect error patterns with autapses in the sensory module (Figure 7 – Figure supplement 2). Below, we have reorganized each Reviewer’s comments and separately addressed them. All changes were shown in red in the manuscript submitted as Related Manuscript File.  

Reviewer #1:

Summary:

Working memory is imperfect - memories accrue errors over time and are biased towards certain identities. For example, previous work has shown memory for orientation is more accurate near the cardinal directions (i.e., variance in responses is smaller for horizontal and vertical stimuli) while being biased towards diagonal orientations (i.e., there is a repulsive bias away from horizontal and vertical stimuli). The magnitude of errors and biases increase the longer an item is held in working memory and when more items are held in working memory (i.e., working memory load is higher). Previous work has argued that biases and errors could be explained by increased perceptual acuity at cardinal directions. However, these models are constrained to sensory perception and do not explain how biases and errors increase over time in memory. The current manuscript builds on this work to show how a two-layer neural network could integrate errors and biases over a memory delay. In brief, the model includes a 'sensory' layer with heterogenous connections that lead to the repulsive bias and decreased error in the cardinal directions. This layer is then reciprocally connected with a classic ring attractor layer. Through their reciprocal interactions, the biases in the sensory layer are constantly integrated into the representation in memory. In this way, the model captures the distribution of biases and errors for different orientations that have been seen in behavior and their increasing magnitude with time. The authors compare the two-layer network to a simpler one-network model, showing that the one-model network is harder to tune and shows an attractive bias for memories that have lower error (which is incompatible with empirical results).

Strengths:

The manuscript provides a nice review of the dynamics of items in working memory, showing how errors and biases differ across stimulus space. The two-layer neural network model is able to capture the behavioral effects as well as relate to neurophysiological observations that memory representations are distributed across the sensory cortex and prefrontal cortex.

The authors use multiple approaches to understand how the network produces the observed results. For example, analyzing the dynamics of memories in the low-dimensional representational space of the networks provides the reader with an intuition for the observed effects.

As a point of comparison with the two-layer network, the authors construct a heterogenous one-layer network (analogous to a single memory network with embedded biases). They argue that such a network is incapable of capturing the observed behavioral effects but could potentially explain biases and noise levels in other sensory domains where attractive biases have lower errors (e.g., color).

The authors show how changes in the strength of Hebbian learning of excitatory and inhibitory synapses can change network behavior. This argues for relatively stronger learning in inhibitory synapses, an interesting prediction.

The manuscript is well-written. In particular, the figures are well done and nicely schematize the model and the results.

Overall:

Overall, the manuscript was successful in building a model that captured the biases and noise observed in working memory. This work complements previous studies that have viewed these effects through the lens of optimal coding, extending these models to explain the effects of time in memory. In addition, the two-layer network architecture extends previous work with similar architectures, adding further support to the distributed nature of working memory representations.

We appreciate the reviewer’s comments that the work successfully explains error patterns of working memory, extends previous models of optimal coding to include temporal effects, and supports the distributed nature of working memory representations. Below, we address the specific concerns of the reviewer.

Weaknesses:

Despite its strengths, the manuscript does have some weaknesses.

Major Point 1: First, as far as we can tell, behavioral data is only presented in schematic form. This means some of the nuances of the effects are lost. It also means that the model is not directly capturing behavioral effects. Therefore, while providing insight into the general phenomenon, the current manuscript may be missing some important aspects of the data.

Relatedly, the models are not directly fit to behavioral data. This makes it hard for the authors to exclude the possibility that there is a single network model that could capture the behavioral effects. In other words, it is hard to support the authors' conclusion that "....these evolving errors...require network interaction between two distinct modules." (from the abstract, but similar comments are made throughout the manuscript). Such a strong claim needs stronger evidence than what is presented. Fitting to behavioral data could allow the authors to explore the full parameter space for both the one-layer and two-layer network architectures.

In addition, directly comparing the ability of different model architectures to fit behavioral data would allow for quantitative comparison between models. Such quantitative comparisons are currently missing from the manuscript.

We agree with the reviewer that incorporating quantitative comparisons to the data will strengthen our results. However, we note the limitations in fitting network models to behavior data. Previous studies employed drift-diffusion models to fit error patterns observed in visual working memory tasks (Panichello, DePasquale et al. 2019, Gu, Lee et al. 2023). In contrast to these phenomenological models, network models have more parameters that can cause overfitting. Consequently, we focused on comparing the qualitative differences between onemodule and two-module networks, examining whether each network can generate the correct shape of bias and variance patterns. In response to the reviewers’ suggestions, we have revised the manuscript to reinforce our claim by providing an intuitive explanation of the qualitative differences between these two models (see response to your Major Point 3) and conducting additional simulations to support our claim that error patterns are consistent under different noise types or levels (see responses to Major Points 2 of Reviewer 2, and Minor point 1 of Reviewer 3).  

Major Point 2: To help broaden the impact of the paper, it would be helpful if the authors provided insight into how the observed behavioral biases and/or network structures influence cognition. For example, previous work has argued that biases may counteract noise, leading to decreased variance at certain locations. Is there a similar normative explanation for why the brain would have repulsive biases away from commonly occurring stimuli? Are they simply a consequence of improved memory accuracy? Why isn't this seen for all stimulus domains?

Previous work has found both diffusive noise and biases increase with the number of items in working memory. It isn't clear how the current model would capture these effects. The authors do note this limitation in the Discussion, but it remains unclear how the current model can be generalized to a multi-item case.

As pointed by the reviewer, attractors counteract noise and lead to reduced variance around the attracting locations. However, most attractor models reporting such effects did not consider the interaction of attractor dynamics with the sensory network. For the repulsive biases considered here, previous studies on the sensory stage have theoretically demonstrated that they could lower the discrimination threshold around cardinal orientations (e.g., see Wei and Stocker, 2017). In Wei and Stocker (2017), the authors showed that this relationship between bias and discrimination threshold was observed across many stimulus modalities. In the present study, we demonstrated that the bias and variability patterns naturally emerged from the underlying neural dynamics. Nonetheless, we also noted that color working memory shows attractive biases, which necessitates further study of the underlying neural mechanisms of color perception. A plausible explanation is that the categorical effect dominates color perception and memory processes, as suggested by existing modelling work (Tajima et al., 2016). 

However, we do note the limitation of our current work that does not capture nuanced error patterns in broader experimental settings, such as variation of perception tasks or memory of multiple items. For instance, while shorter stimulus presentations with no explicit delay lead to larger biases experimentally, our current model, which starts activities from a flat baseline, shows an increase in bias throughout the stimulus presentation. Additionally, the error variance during stimulus presentation is almost negligible compared to that during the delay period, as the external input overwhelms the internal noise. These mismatches during stimulus presentation have minimal impact on activities during the delay period when the internal dynamics dominate. Nonetheless, the model needs further refinement to accurately reproduce activities during stimulus presentation, possibly by incorporating more biologically plausible baseline activities. Also, a recent Bayesian perception model suggested different types of noise like external noise or variations in loss functions that adjust tolerance to small errors may help explain various error patterns observed across different modalities (Hahn and Wei, 2024). Even for memories involving multiple items, noise can be critical in determining error patterns, as encoding more items might be equivalent to higher noise for each individual item (Chunharas, Rademaker et al. 2022).

To make this limitation clear, we included the above response in a new paragraph on limitations and future directions in the Discussion (2nd paragraph in p. 11). Also, we modified the text that previously described that our model can “explain error patterns in both perception and working memory tasks” in p. 3 and p. 5 as

“explain error patterns in working memory tasks that are similar to those observed in perception tasks.”

And we added the bias and variance pattern right after the stimulus offset in Figure 4C,D with the following note in p. 6:

“Note that the variance of errors is nearly zero during stimulus presentation because the external input overwhelms internal noise, which does not fully account for the variability observed during perception tasks (see Discussion).”

Major Point 3: The role of the ring attractor memory network isn't completely clear. There is noise added in this stage, but how is this different from the noise added at the sensory stage? Shouldn't these be additive? Is the noise necessary?  

Similarly, it isn't clear whether the memory network is necessary - can it be replaced by autapses (self-connections) in the sensory network to stabilize its representation? In short, it would be helpful for the authors to provide an intuition for why the addition of the memory network facilitates the repulsive bias.

Internal noise in the circuits is necessary to replicate the variability of the readout in estimating the stimulus because our model did not incorporate external noise (i.e., noise associated with the stimulus). We note the distinct noise implementation in both extension of the previous Bayesian model (Fig. 2) and the network models (Fig. 3 and beyond). In Fig. 2, we followed previous studies by employing static tuning curves for the sensory module and Poisson noise to account for variability in the perception stage. In the memory stage, sensory output undergoes the addition of constant Gaussian noise, replicating the diffusion process along the memory manifolds as shown in traditional memory network models. In the network models, we do consider the same noise in both sensory and memory modules, subjecting all units to Poisson noise to simulate neuronal spiking variability. In the network models, the two modules dynamically interact, which warp the energy landscape and generate uneven noise coefficients along the memory manifold, reminiscent of the conditions shown in Fig. 1. 

From the bias and variance patterns, we can infer two requirements the network to fulfill – one is efficient coding suggested by sensory perception stage and the other is memory maintenance. The former is achieved by realizing the previous Bayesian models in the sensory networks with specific heterogeneous connections. In our work, the latter is achieved by strong recurrent connections to sustain persistent activity during the delay period. On the other hand, as the reviewer noted, memory can be maintained through autapses in the sensory network, which is equivalent to elongating intrinsic time constants of individual units (Seung, Lee et al. 2000). We simulated such sensory network and showed the results in Figure 7 – Figure Supplement 2. As shown in the figure, a larger time constant also slows down the increase in bias significantly, which can be deduced from Eq. 20. 

When memory is maintained through strong recurrent connections, there are two possible scenarios, one-module network combining both efficient coding and memory maintenance (Fig. 8), or two-module network satisfying each condition in different modules (Fig. 7). In both networks, heterogeneous connections achieving efficient coding shape drift and diffusion dynamics similarly as illustrated in Figure 9 (previous Figure 7 – Supplement 1). Discrete attractors are formed near oblique orientations, inducing an increase of repulsive bias during the delay period. Also, noise coefficient is lowest at cardinal orientations. However, there is a difference in the asymmetry degrees of the drift and diffusion at cardinal and oblique orientations the one-module network shows larger asymmetry in potential energy, while the two-module network shows larger asymmetry in the noise coefficient. These varying degrees of heterogeneity in drift and diffusion lead to qualitative differences in bias and variance patterns in estimation. Shallower potential differences with more asymmetrical noise coefficients result in correct bias and variance patterns in the two-module network, while the opposite leads to flipped variance patterns in the one-module network.  

An intuitive explanation of how connectivity heterogeneity differentially affects the asymmetry degrees of drift and diffusion in one-module and two-module networks is detailed in our response to Major Point 3 of Reviewer 2. In summary, separating the memory module from the sensory module imposes an additional degree of freedom, allowing for more flexible control over drift and diffusion, thereby bias and variance patterns. To clarify this, we have added simulations in Figure 6 and Figure 9 and provided an intuitive explanation in the accompanying texts in pp. 6-7 and p. 9. 

Minor Point 1: The code is stated to be available on GitHub, but I could not access it.

Thank you for pointing it out. The repository is now publicly available.

Minor Point 2: The legend for late/mid/early is in an odd place in Figure 1, as it is in panel E where you can't see the difference between the lines. We would suggest moving this to another panel where the different time points are clear. In general, we would suggest adding more text (legends and titles) to the figure to help the reader understand the figures without having to refer to the details in the text and/or figure legends.

We have now moved the legend to panel B where late/mid/early is first introduced. Also, we added more text to the figure legend (Figure 3,4,5,8). 

Minor Point 3: The last line of the first paragraph of the Introduction ends awkwardly. I assume it's referring to indirect evidence for dynamics in memory?

Thank you. We have modified the sentence as follows:

“For instance, biases of errors, the systematic deviation from the original stimuli, observed in estimation tasks have been used as indirect evidence to infer changes in internal representations of stimuli.”

Minor Point 4: Similarly, the first line of the second paragraph of the Introduction was also awkward. Specifically, the clause "..., such as nonuniform stimulus distribution in nature." Seems to be missing a 'the' before 'nonuniform'.

We have modified the sentence as follows:

“One important source of biases is adaptation to environmental statistics, such as the nonuniform stimulus distribution found in nature or the limited range in specific settings.”

Reviewer #2:

In this manuscript, Yang et al. present a modeling framework to understand the pattern of response biases and variance observed in delayed-response orientation estimation tasks. They combine a series of modeling approaches to show that coupled sensory-memory networks are in a better position than single-area models to support experimentally observed delay-dependent response bias and variance in cardinal compared to oblique orientations. These errors can emerge from a population-code approach that implements efficient coding and Bayesian inference principles and is coupled to a memory module that introduces random maintenance errors. A biological implementation of such operation is found when coupling two neural network modules, a sensory module with connectivity inhomogeneities that reflect environment priors, and a memory module with strong homogeneous connectivity that sustains continuous ring attractor function. Comparison with single-network solutions that combine both connectivity inhomogeneities and memory attractors shows that two-area models can more easily reproduce the patterns of errors observed experimentally. This, the authors take as evidence that a sensory-memory network is necessary, but I am not convinced about the evidence in support of this "necessity" condition. A more in-depth understanding of the mechanisms operating in these models would be necessary to make this point clear.

Strengths:

The model provides an integration of two modeling approaches to the computational bases of behavioral biases: one based on Bayesian and efficient coding principles, and one based on attractor dynamics. These two perspectives are not usually integrated consistently in existing studies, which this manuscript beautifully achieves. This is a conceptual advancement, especially because it brings together the perceptual and memory components of common laboratory tasks.

The proposed two-area model provides a biologically plausible implementation of efficient coding and Bayesian inference principles, which interact seamlessly with a memory buffer to produce a complex pattern of delay-dependent response errors. No previous model had achieved this.

We appreciate the reviewer’s comments that the work is a conceptual advancement, combining Bayesian perception models and attractor memory models, and produces error patterns which wasn’t achieved by previous models. Below, we address the specific concerns of the reviewer.

Major Point 1: The correspondence between the various computational models is not fully disclosed. It is not easy to see this correspondence because the network function is illustrated with different representations for different models and the correspondence between components of the various models is not specified. For instance, Figure 1 shows that a specific pattern of noise is required in the low-dimensional attractor model, but in the next model in Figure 2, the memory noise is uniform for all stimuli. How do these two models integrate? What element in the population-code model of Figure 2 plays the role of the inhomogeneous noise of Figure 1? Also, the Bayesian model of Figure 2 is illustrated with population responses for different stimuli and delays, while the attractor models of Figures 3 and 4 are illustrated with neuronal tuning curves but not population activity. In addition, error variance in the Bayesian model appears to be already higher for oblique orientations in the first iteration whereas it is only first shown one second into the delay for the attractor model in Figure 4. It is thus unclear whether variance inhomogeneities appear already at the perceptual stage in the attractor model, as it does in the population-code model. Of course, correspondences do not need to be perfect, but the reader does not know right now how far the correspondence between these models goes.

Thank you for pointing out the lack of clarity in the correspondence between different models. We note the distinct noise implementation in extension of the previous Bayesian model (Fig. 2) and the network models (Fig. 3 and beyond). In Fig. 2, we followed previous studies by employing static tuning curves for the sensory module and Poisson noise to account for variability in the perception stage. In the memory stage, sensory output undergoes the addition of constant Gaussian noise, replicating the diffusion process along the memory manifolds as shown in traditional memory network models. In the network models in Fig. 3 and beyond, we do consider the same noise in both sensory and memory modules, subjecting all units to Poisson noise to simulate neuronal spiking variability. In the network models, the two modules dynamically interact, which warp the energy landscape and generate uneven noise coefficients along the memory manifold, reminiscent of the conditions shown in Fig. 1. 

However, we do note the limitation of the current study which cannot fully replicate behavior patterns observed in variation of perception tasks. For instance, while shorter stimulus presentations with no explicit delay lead to larger biases experimentally, our current model, which starts activities from a flat baseline, shows an increase in bias throughout the stimulus presentation. Additionally, the error variance during stimulus presentation is almost negligible compared to that during the delay period, as the external input overwhelms the internal noise. These mismatches during stimulus presentation have minimal impact on activities during the delay period when the internal dynamics dominate. Nonetheless, the model needs further refinement to accurately reproduce activities during stimulus presentation, possibly by incorporating more biologically plausible baseline activities. To make this limitation clear, we included the above response in a new paragraph on limitations and future directions in the Discussion (2nd paragraph in p. 11). Also, we modified the text that previously described that our model can “explain error patterns in both perception and working memory tasks” in p. 3 and p. 5 as “explain error patterns in working memory tasks that are similar to those observed in perception tasks.”

And we added the bias and variance pattern right after the stimulus offset in Figure 4C,D with the following note in p. 6:

“Note that the variance of errors is nearly zero during stimulus presentation because the external input overwhelms internal noise, which does not fully account for the variability observed during perception tasks (see Discussion).”

Major Point 2: The manuscript does not identify the mechanistic origin in the model of Figure 4 of the specific noise pattern that is required for appropriate network function (with higher noise variance at oblique orientations). This mechanism appears critical, so it would be important to know what it is and how it can be regulated. In particular, it would be interesting to know if the specific choice of Poisson noise in Equation (3) is important. Tuning curves in Figure 4 indicate that population activity for oblique stimuli will have higher rates than for cardinal stimuli and thus induce a larger variance of injected noise in oblique orientations, based on this Poissonnoise assumption. If this explanation holds, one wonders if network inhomogeneities could be included (for instance in neural excitability) to induce higher firing rates in the cardinal/oblique orientations so as to change noise inhomogeneities independently of the bias and thus control more closely the specific pattern of errors observed, possibly within a single memory network.

The specific pattern of noise coefficient, lower variability at cardinal orientations in the network models, inherited that of the previous Bayesian perception models (Wei and Stocker, 2017). Either in one-module or two-module networks, the specific pattern of heterogeneous connections induces more neurons tuned to cardinal orientations with narrower tuning widths. Such sparser representation near cardinal stimuli generates lower noise variability even with constant Gaussian noise. This is verified in Eq. 21 in Methods, showing the derivation of noise coefficients – with constant Gaussian noise, Eq. 21 is modified as 

because . Thus, 𝒟(𝜃) is inversely proportional to , which reflects the length travelled on the stable trajectory 𝒔𝒔‾(𝜃𝜃) when θ increases by one unit. For sparser representation,   becomes larger and 𝒟(𝜃) is reduced. Intuitively, with more neurons tuned to cardinal stimuli, noise is averaged and reduced. In sum, the heterogeneous connection induces the specific noise coefficient, and the choice of Poisson-like noise is not essential, although it facilitates the correct variance pattern. To clarify this point, we have added the results of using uniform Gaussian noise in new Figure 5 – Figure Supplement 2 and Figure 9 – Figure Supplement 1.

Major point 3: The main conclusion of the manuscript, that the observed patterns of errors "require network interaction between two distinct modules" is not convincingly shown. The analyses show that there is a quantitative but not a qualitative difference between the dynamics of the single memory area compared to the sensory-memory two-area network, for specific implementations of these models (Figure 7 - Figure Supplement 1). There is no principled reasoning that demonstrates that the required patterns of response errors cannot be obtained from a different memory model on its own. Also, since the necessity of the two-area configuration is highlighted as the main conclusion of the manuscript, it is inconvenient that the figure that carefully compares these conditions is in the Supplementary Material.

Following the suggestion by the reviewer, we moved Figure 7 – Figure supplement 1 as new Figure 9. As noted by the reviewer, drift dynamics and diffusion projected onto the lowdimensional memory manifold have similar shapes in both one-module and two-module networks, with the lowest potential and highest noise coefficient observed at the oblique orientations. However, there is a difference in the asymmetry degrees of the drift and diffusion at cardinal and oblique orientations: the one-module network shows larger asymmetry in potential energy, while the two-module network shows larger asymmetry in the noise coefficient. These varying degrees of heterogeneity in drift and diffusion lead to qualitative differences in bias and variance patterns in estimation. Shallower potential differences with more asymmetrical noise coefficients result in correct bias and variance patterns in the two-module network, while the opposite leads to flipped variance patterns in the one-module network.  

To intuitively understand how connectivity heterogeneity differentially affects the asymmetry degrees of drift and diffusion in one-module and two-module networks, consider a simple case where only the excitatory connection is heterogeneous, denoted as α. The asymmetry of diffusion reflects the degree of heterogeneity in either the sensory or memory modules. The noise coefficient derived from the low-dimensional projection is mainly determined by the heterogeneity of . While the one-module network, with a much lower α, shows almost flat , the two-module network shows more prominent asymmetry in with a larger α in the sensory module.  

On the other hand, the asymmetry in the potential energy is influenced differently by the connectivity heterogeneity of the sensory module and that of the memory module. For memory maintenance, overall recurrent connections need to be strong enough to overcome intrinsic decay, simplifying to w = 1. In the one-module network, α in the memory module creates potential differences at cardinal and oblique orientations as 1± α. On the other hand, in the two-module network, with w = 1 fulfilled by the memory module, α in the sensory module acts as a perturbation. The effect of α is modulated by the connectivity strengths between sensory and memory module, denoted by γ. Potential differences at cardinal and oblique orientations can be represented as 1± γα. While both α and γ determine the energy level, the noise coefficient less depends on γ (see response to your Major Point 4). Thus, even for relatively larger α in the sensory module leading to more asymmetrical noise coefficients, the potential difference could be shallower in the two-module network with small γ<1. 

In sum, in the two-module network, there is an additional degree of freedom, connectivity strengths between sensory and memory modules, which provides the flexibility to control drift and diffusion separately, unlike in the one-module network. To clarify this, we have added simulations in Figure 6 and Figure 9 and provided an intuitive explanation in the accompanying texts in pp. 6-7 and p. 9.

Major Point 4: The proposed model has stronger feedback than feedforward connections between the sensory and memory modules. This is not a common assumption when thinking about hierarchical processing in the brain, and it is not discussed in the manuscript.

As noted in the previous response, the connectivity strengths between the sensory and memory modules, denoted as γ, are important parameters determining the qualitative features of bias and variance patterns. γ corresponds to the product of Jf and Jb, feedforward and feedback strengths, and our additional simulation shows that the bias and variance patterns remain similar for a fixed γ. Note that further simulation revealed that the heterogeneity degree, α, and the intermodal connectivity strengths, γ, influence the drift and diffusion terms differently. As this result highlights the advantage of the two-module network, we moved the dependence of error patterns on intermodal connectivity strengths to the main figure (previous Figure 5 – Figure supplement 2), which now includes more simulations showing bias and variance patterns for different Jf and Jb and for different α and Jb (new Figure 6). 

Minor Point 1: page 11: "circular standard deviation of sigma_theta = 1.3º at cardinal orientations" but in Figure 2 we see sigma_theta = 2º at cardinal orientations.

The circular standard deviation of 𝜎𝜎𝜃𝜃 = 1.3º refers to the standard deviation of the sensory module output in iteration 1, that is, before feeding into the memory module to complete this iteration. In figure 2, the standard deviation plotted is that of the output of the memory module, which has a Gaussian memory noise with standard deviation 1.3º added on top of the sensory output. Hence we see a standard deviation of √(1.32 + 1.32) = 1.84º which seems close to 2º in the figure. We added a sentence in this paragraph of Methods (p. 13) to avoid confusion.

Minor Point 2: equation (19): What does the prime of ||s'(theta)|| mean?

The prime represents taking the derivative with respect to θ:

reflects the length travelled on the stable trajectory when θ increases by one unit. As we plotted in Figure 9 and Figure 5 – Figure supplement 2, we clarified it in the legend.

Minor Point 3: page 15: "The Fisher information (F) is estimated by assuming that the likelihood function p(r|theta) is Gaussian", but the whole point of Wei and Stocker (2015) and your Figure 2 is that likelihoods are skewed in these networks. This could be clarified.

Thank you for pointing out the lack of clarity. In Wei and Stocker (2015) and our Figure 2, the likelihood is skewed with respect to 𝜃 (note the horizontal axes). However, in the Methods section, we assumed the distribution function 𝑝(𝑟|𝜃) is Gaussian with respect to 𝑟𝑟 when 𝜃 is considered fixed:

where . The distribution function is skewed with respect to 𝜃 because the tuning curves are skewed with respect to 𝜃 (see Figure 4B). We have clarified our assumption in p. 16 to avoid confusion.

Reviewer #3:

Summary:

The present study proposes a neural circuit model consisting of coupled sensory and memory networks to explain the circuit mechanism of the cardinal effect in orientation perception which is characterized by the bias towards the oblique orientation and the largest variance at the oblique orientation.

Strengths:

The authors have done numerical simulations and preliminary analysis of the neural circuit model to show the model successfully reproduces the cardinal effect. And the paper is wellwritten overall. As far as I know, most of the studies on the cardinal effect are at the level of statistical models, and the current study provides one possibility of how neural circuit models reproduce such an effect.

We appreciate the reviewer’s comments that the work successfully reproduces error patterns through circuit models, advancing beyond previous statistical models. Below, we address the specific concerns of the reviewer.

Weaknesses:

There are no major weaknesses and flaws in the present study, although I suggest the author conduct further analysis to deepen our understanding of the circuit mechanism of the cardinal effects. Please find my recommendations for concrete comments.

Minor Point 1: Likely, the interplay of the potential function (Figure 5D) and the noise amplitude (Figure 5C) in the memory network is the key to reproducing the cardinal effect. For me, it is obvious to understand the spatial profile of the potential function as what it currently looks like (Figure 5D), while I haven't had an intuitive understanding of how the spatial profile of noise structure emerges from the circuit model. Therefore I suggest the authors provide a more comprehensive analysis, including theory and simulation, to demonstrate how the noise structure depends on the network parameters. I am concerned about whether the memory network can still reproduce the minimal variance at the cardinal orientation if we reduce the Fano factor of single neuron variabilities. In this case, the shape of the potential function will be dominant in determining the variance over orientation (Figure 5F) and the result might be reverted.

Thank you for the suggestion. Either in one-module or two-module networks, the specific pattern of heterogeneous connections induces more neurons tuned to cardinal orientations with narrower tuning widths. Such sparser representation near cardinal stimuli generates lower noise variability even with constant Gaussian noise, which is now added in Figure 5 – Figure Supplement 2. We also showed that the distinctive error patterns in one-module and two-module networks are maintained under Gaussian noise with varying amplitude in Figure 9 – Figure supplement 1.

Minor Point 2: In addition, it is interesting to show how the representation of the sensory module looks like, e.g., plotting the figures similar to Figures B-F but from the sensory module. I feel the sensory module doesn't have a result similar to Figure 5F. Is it?

Yes, decoded error patterns obtained from the sensory module are similar to the results obtained from the memory module. We have added Figure 4 – Figure supplement 1 to show that our conclusions remain valid when decoding from the sensory module.

Minor point 3: Last but not least, I have a conceptual question about the presentation mechanism in the proposed circuit model. The present study refers to Wei, et al., 2015 and 2017 about the statistical model mechanism of the cardinal effect. If I remember correctly, Wei's papers considered joint encoding and decoding processes to render the cardinal effect. Can the authors regard the processes in the proposed circuit model with the stages in the statistical model? Or at least the authors should discuss this link in the Discussions.

We now included a mention of using a population vector decoder that mimics Bayesian optimal readout in the Result section (p. 6), in addition to the Discussion and Methods. However, we acknowledge that this decoder is only optimal under a specific loss function. A recent Bayesian perception model suggested different types of noise like external noise or variations in loss functions that adjust tolerance to small errors may help explain various error patterns observed across different modalities (Hahn and Wei, 2024). We have now added this limitation in the Discussion, along with the inconsistency of the current model with experimental observations during perception tasks and future directions (p. 11).

Author response:

Reviewer #1 (Public Review):

In this study, Girardello et al. use proteomics to reveal the membrane tension sensitive caveolin-1 interactome in migrating cells. The authors use EM and surface rendering to demonstrate that caveolae formed at the rear of migrating cells are complex membrane-linked multilobed structures, and they devise a robust strategy to identify caveolin-1 associated proteins using APEX2-mediated proximity biotinylation. This important dataset is further validated using proximity ligation assays to confirm key interactions, and follows up with an interrogation of a surprising relationship between caveolae and RhoGTPase signalling, where caveolin-1 recruits ROCK1 under high membrane tension conditions, and ROCK1 activity is required to reform caveolae upon reversion to isotonic solution. However, caveolin-1 recruits the RhoA inactivator ARHGAP29 when membrane tension is low and ARHGAP29 overexpression leads to disassembly of caveolae and reduced cell motility. This study builds on previous findings linking caveolae to positive feedback regulation of RhoA signalling, and provides further evidence that caveolae serve to drive rear retraction in migration but also possess an intrinsic brake to limit RhoA activation, leading the authors to suggest that cycles of caveolae assembly and disassembly could thereby be central to establish a stable cell rear for persistent cell migration

A major strength of the manuscript is the robust proteomic dataset. The experimental set up is well defined and mostly well controlled, and there is good internal validation in that the high abundance of core caveolar proteins in low membrane tension (isotonic) conditions, and absence under high membrane tension (brief hypo-osmotic shock) conditions, correlating very well with previous finding. The data could however be better presented to show where statically robust changes occur, and supplementary information should include a table of showing abundance. It's very good to see a link to PRIDE, providing a useful resource for the community.

We thank the reviewer for the positive feedback. We have included the outputs from the search engine in Supplementary File 1.

The authors detail several known interactions and their mechanosensitivty, but also report new interactors of caveolin-1. Several mechanosensitive interactions of caveolin-1 take place at the cell rear, but others are more diffuse across the cell looking at the PLA data (e.g FLN1, CTTN, HSPB1; Figure 4A-F and Figure 4 supplement 1). It is interesting to speculate that those at the cell rear are involved in caveolae, whilst others are linked specifically to caveolin-1 (e.g. dolines). PLA or localisation analysis with Cavin1/PTRF may be able to resolve this and further specify caveolae versus non-caveolae mechanosensitive interactions.

We thank the reviewer for this interesting idea. It is true that many if not most proteins we identified to be associated with Cav1 are not restricted to the cell rear. To analyse to what extent the identified proteins interact with Cav1 at the rear we reanalysed our PLA data for some of the antibody combinations we looked at. This new analysis is now shown in Fig 5G. As expected, for Cav1/PTRF and Cav1/EHD2 most PLA dots (70-80%) were found at the rear. This rear bias is also evident from the representative images we show in the Figure panels 5A and 5E. On the contrary, much fewer PLA dots (~40%) were rear-localised for Cav1/CTTN and Cav1/FLNA antibody combinations. This reflects the much broader cellular distribution of these proteins compared to the core caveolae proteins, and might suggest that there are generally few links between caveolae and cortical actin. However, it is also possible that such links/interactions are more difficult to detect using PLA (because of the extended distance between caveolae and the actin cortex, or because of steric constraints).

The Cav1/ARHGAP29 influence on YAP signalling is interesting, but appear to be quite isolated from the rest of the manuscript. Does overexpression of ARHGAP29 influence YAP signalling and/or caveolar protein expression/Cav1pY14?

Our data and published work originally prompted us to speculate that there is a potential functional link between Cav1, YAP, and ARHGAP29. In an attempt to address this we have performed several Western blots on cell lysates from cells overexpressing ARHGAP29. We did not see major changes in Cav1 Y14 phosphorylation levels in cells overexpressing ARHGAP29, and YAP and pYAP levels also remained unchanged (not shown). In addition, based on previous literature 1,2 we expected to see an effect on ARHGAP29 mRNA levels and YAP target gene transcripts in Cav1 siRNA transfected cells. To our surprise, the mRNA levels of three independent YAP target genes and ARHGAP29 were unchanged in Cav1 siRNA treated cells (this is now shown in Figure 6 Figure Supplement 1). Our data therefore suggest that in RPE1 cells, the connection between Cav1 and ARHGAP29 is independent of YAP signalling, and that the increase in ARHGAP29 protein levels observed in Cav1 siRNA cells is due to some unknown post-translational mechanism.

ARHGAP29 and RhoA/ROCK1 related observations are very interesting and potentially really important. However, the link between ARHGAP29 and caveolae is not well established (other than in proteomic data). PLA or FRET could help establish this.

We agree that the physical and functional link between caveolae (or Cav1) and ARHGAP29 was not well worked out in the original manuscript. In an attempt to address this we have performed PLA assays in GFP-ARHGAP29 transfected cells (as we did not find a suitable ARHGAP29 antibody that works reliably in IF) using anti-Cav1 and anti-GFP antibodies. The PLA signal we obtained for Cav1 and ARHGAP29 was not significantly different to control PLA experiments. There was very little PLA signal to start with. This is not surprising given that ARHGAP29 localisation is mostly diffuse in the cytoplasm, whilst Cav1 is concentrated at the rear. In addition, in cases where we do see ARHGAP29 localisation at the cell cortex, Cav1 tends to be absent (this is now shown in Figure 6 – Figure Supplement 2E). In other words, with the tools we have available, we see little colocalization between Cav1 and ARHGAP29 at steady state. Altogether we speculate that ARHGAP29, through its negative effect on RhoA, flattens caveolae at the membrane or interferes with caveolae assembly at these sites.

This of course prompts the question why ARHGAP29 was identified in the Cav1 proteome with such specificity and reproducibility in the first place? This can be explained by the way APEX2 labeling works. Proximity biotinylation with APEX2 is extremely sensitive and restricted to a labelling radius of ~20 nm 3. The labeling reaction is conducted on live and intact cells at room temperature for 1 min. Although 1 min appears short, dynamic cellular processes occur at the time scale of seconds and are ongoing during the labelling reaction. It is conceivable that within this 1 min time frame, ARHGAP29 cycles on and off the rear membrane (kiss and run). This allows ARHGAP29 to be biotinylated by Cav1-APEX2, resulting in its identification by MS. We have included this in the discussion section.

The relationship between ARHGAP29 and RhoA signalling is not well defined. Is GAP activity important in determining the effect on migration and caveolae formation? What is the effect on RhoA activity? Alternatively, the authors could investigate YAP dependent transcriptional regulation downstream of overexpression.

We have addressed this point using overexpression and siRNA transfections. We overexpressed ARHGAP29 or ARHGAP29 lacking its GAP domain and performed WB analysis against pMLC (which is a commonly used and reliable readout for RhoA and myosin-II activity). Much to our surprise, overexpression of ARHGAP29 increased (rather than decreased) pMLC levels, partially in a GAP-dependent manner (see Author response image 1). This is puzzling, as ARHGAP29 is expected to reduce RhoA-GTP levels, which in turn is expected to reduce ROCK activity and hence pMLC levels. In addition, and also surprisingly, siRNA-mediated silencing of ARHGAP29 did not significantly change pMLC levels. By contrast, pMLC levels were strongly reduced in Cav1 siRNA treated cells (this is shown in Fig. 6A and 6B in the revised manuscript). These new data underscore the important role of caveolae in the control of myosin-II activity, but do not allow us to draw any firm conclusions about the role of ARHGAP29 at the cell rear.

Author response image 1.

Overexpression of ARHGAP29 reduces, rather than increases pMLC in RPE1 cells.

We are uncertain as to how to interpret the ARHGAP29 overexpression data presented in Author response image 1 and therefore decided not to include it in the manuscript. One possibility is that inactivation of RhoA below a certain critical threshold causes other mechanisms to compensate. For instance, the activity of alternative MLC kinases such as MLCK could be enhanced under these conditions. Another possibility is that ARHGAP29 controls MLC phosphorylation indirectly. For instance, it has been shown that ARHGAP29 promotes actin destabilization through inactivating LIMK/cofilin signalling 1. In agreement with this, we find that overexpression of ARHGAP29 reduces p-cofilin (serine 3) levels (see Author response image 2). Since cofilin and MLC crosstalk 4, it is possible that increased pMLC levels are the result of a feedback loop that compensates for the effect of actin depolymerisation. This is now discussed in the discussion section. Whichever the case, we hope the reviewers understand that deeper mechanistic insight into the intricate mechanisms of Rho signalling at the cell rear are beyond the scope of this manuscript.

Author response image 2.

Overexpression of ARHGAP29 reduces p-cofilin levels in RPE1.

Reviewer #2 (Public Review):

Girardello et al investigated the composition of the molecular machinery of caveolae governing their mechano-regulation in migrating cells. Using live cell imaging and RPE1 cells, the authors provide a spatio-temporal analysis of cavin-3 distribution during cell migration and reveal that caveolae are preferentially localized at the rear of the cell in a stable manner. They further characterize these structures using electron tomography and reveal an organization into clusters connected to the cell surface. By performing a proteomic approach, they address the interactome of caveolin-1 proteins upon mechanical stimulation by exposing RPE1 cells to hypo-osmotic shock (which aims to increase cell membrane tension) or not as a control condition. The authors identify over 300 proteins, notably proteins related to actin cytoskeleton and cell adhesion. These results were further validated in cellulo by interrogating protein-protein interactions using proximity ligation assays and hypo-osmotic shock. These experiments confirmed previous data showing that high membrane tension induces caveolae disassembly in a reversible manner. Eventually, based on literature and on the results collected by the proteomic analysis, authors investigated more deeply the molecular signaling pathway controlling caveolae assembly upon mechanical stimuli. First, they confirm the targeting of ROCK1 with Caveolin-1 and the implication of the kinase activity for caveolae formation (at the rear of the cell). Then, they show that RhoGAP ARHGAP29, a factor newly identified by the proteomic analysis, is also implicated in caveolae mechano-regulation likely through YAP protein and found that overexpression of RhoGAP ARHGAP29 affects cell motility. Overall, this paper interrogated the role of membrane tension in caveolae located at the rear of the cell and identified a new pathway controlling cell motility.

Strengths:

Using a proximity-based proteomic assay, the authors reveal the protein network interacting with caveolae upon mechanical stimuli. This approach is elegant and allows to identify a substantial new set of factors involved in the mechano-regulation of caveolin-1, some of which have been verified directly in the cell by PLA. This study provides a compelling set of data on the interactions between caveolae and its cortical network which was so far ill-characterized.

We thank the reviewer for this positive feedback.

Weaknesses:

The methodology demonstrating an impact of membrane tension is not precise enough to directly assess a direct role on caveolae at a subcellular scale, that is between the front and the rear of the cell. First, a better characterization of the "front-rear" cellular model is encouraged.

We agree with the reviewer that a quantitative analysis of the caveolae front-rear polarity would strengthen our conclusions. To address this, we have analysed the localisation of Cav1 and cavins in detail and in a large pool of cells, both in fixed and live cells. Our quantification clearly shows that Cav1 and cavins are enriched at the cell rear. This is now shown in Figure 1 and Figure 1 - Figure Supplement 1. To demonstrate that Cav1/cavins are truly rear-localised we analysed live migrating cells expressing tagged Cav1 or cavins. This analysis, which was performed on several individual time lapse movies, showed that caveolae rear localisation is remarkably stable (e.g. Figure 1C and 1D). We also present novel data panels and movies showing caveolae dynamics during rear retractions, in dividing cells, and in cells that polarise de novo. This new data is now described in the first paragraph of the results section.

Secondly, authors frequently present osmotic shock as "high membrane tension" stimuli. While osmotic shock is widely used in the field, this study is focused only on caveolae localized at the rear of cell and it remains unclear how the level of a global mechanical stimuli triggered by an osmotic shock could mimic a local stimuli.

We agree with the reviewer that osmotic shock will cause a global increase in membrane tension and therefore is only of limited value to understand how membrane tension is regulated at the rear, and how caveolae respond to such a local stimulus. It was not our aim nor is it our expertise to address such questions. To answer this sophisticated optogenetic approaches or localised membrane tension measurements (e.g. through the use of the Flipper-TR probe) are needed. It is beyond the scope of this manuscript to perform such experiments. However, given the strong enrichment of caveolae at the cell rear, we believe it is justified to propose that the changes we observe in the proteome do (mostly) reflect changes in caveolae at the rear. We have now included several quantifications on fixed cells, live cells, and PLA assays to support that caveolae are highly enriched at the rear. In addition, and importantly, a recent preprint by the Roux lab shows that membrane tension gradients indeed exist in many migrating and non-migrating cells 5. Using very similar hypotonic shock assays, the Caswell lab also showed that low membrane tension at the rear is required for caveolae formation 6. We have included a section in the discussion in which we elaborate on how membrane tension is controlled in migrating cells, and how it might regulate caveolae rear localisation.

In the present case, it remains unknown the extent to which this mechanical stress is physiologically relevant to mimic mechanical forces applied at the rear of a migrating cell.

This is true. Our study does not address the nature of mechanical forces at the cell rear. This a complex subject that is technically challenging to address, and therefore is beyond the scope of this manuscript.

Some images are not satisfying to fully support the conclusions of the article.

We agree that some of the images, in particular the ones presented for the PLA assays, do not always show a clear rear localisation of caveolae. We have explained above why this is the case. We hope that our new quantitative measurements, movies and figure panels, addresses the reviewer’s concern.

At this stage, the lack of an unbiased quantitative analysis of the spatio-temporal analysis of caveolae upon well-defined mechanical stimuli is also needed.

These are all very good points that were previously addressed beautifully by the Caswell group 6. To address this in part in our RPE1 cell system, we imaged RPE1 cells exposed to the ROCK inhibitor Y27632 (see Author response image 3). The data shows that cell rear retraction is impeded in response to ROCK inhibition, which is in line with several previous reports. Cavin-1 remained mostly associated with the cell rear, although the distribution appeared more diffuse. We believe this data does not add much new insight into how caveolae function at the rear, and hence was not included in the manuscript.

Author response image 3.

Effect of ROCK inhibition on cavin1 rear localisation and rear retraction. Cells were imaged one hour after the addition of Y27632.

Cells on images, in particular Figure 1, are difficult to see. Signal-to noise ratio in different cell area could generate a biased. Since there is inconsistency between caveolae density and localization between Figures, more solid illustrations are needed along quantitative analysis.

As mentioned above, we have carefully analysed the localisation of caveolae in fixed cells (using Cav1 and cavin1 antibodies as well as Cav1 and cavin fusion proteins) and in live cells transfected with various different caveolae proteins. The analysis clearly demonstrates an enrichment of caveolae at the rear (Figure 1 and Figure 1 – Figure Supplement 1). Our tomography and TEM data supports this as well (Figure 2).

References:

1. Qiao Y, Chen J, Lim YB, et al. YAP Regulates Actin Dynamics through ARHGAP29 and Promotes Metastasis. Cell reports. 2017;19(8):1495-1502.

2. Rausch V, Bostrom JR, Park J, et al. The Hippo Pathway Regulates Caveolae Expression and Mediates Flow Response via Caveolae. Curr Biol. 2019;29(2):242-255 e246.

3. Hung V, Udeshi ND, Lam SS, et al. Spatially resolved proteomic mapping in living cells with the engineered peroxidase APEX2. Nat Protoc. 2016;11(3):456-475.

4. Wiggan O, Shaw AE, DeLuca JG, Bamburg JR. ADF/cofilin regulates actomyosin assembly through competitive inhibition of myosin II binding to F-actin. Dev Cell. 2012;22(3):530-543.

5. Juan Manuel García-Arcos AM, Julissa Sánchez Velázquez, Pau Guillamat, Caterina Tomba, Laura Houzet, Laura Capolupo, Giovanni D’Angelo, Adai Colom, Elizabeth Hinde, Charlotte Aumeier, Aurélien Roux. Actin dynamics sustains spatial gradients of membrane tension in adherent cells. bioRxiv 20240715603517. 2024.

6. Hetmanski JHR, de Belly H, Busnelli I, et al. Membrane Tension Orchestrates Rear Retraction in Matrix-Directed Cell Migration. Dev Cell. 2019;51(4):460-475 e410.

7. Tsai TY, Collins SR, Chan CK, et al. Efficient Front-Rear Coupling in Neutrophil Chemotaxis by Dynamic Myosin II Localization. Dev Cell. 2019;49(2):189-205 e186.

8. Mueller J, Szep G, Nemethova M, et al. Load Adaptation of Lamellipodial Actin Networks. Cell. 2017;171(1):188-200 e116.

9. De Belly H, Yan S, Borja da Rocha H, et al. Cell protrusions and contractions generate long-range membrane tension propagation. Cell. 2023.

10. Matthaeus C, Sochacki KA, Dickey AM, et al. The molecular organization of differentially curved caveolae indicates bendable structural units at the plasma membrane. Nat Commun. 2022;13(1):7234.

11. Sinha B, Koster D, Ruez R, et al. Cells respond to mechanical stress by rapid disassembly of caveolae. Cell. 2011;144(3):402-413.

12. Lieber AD, Schweitzer Y, Kozlov MM, Keren K. Front-to-rear membrane tension gradient in rapidly moving cells. Biophysical journal. 2015;108(7):1599-1603.

13. Shi Z, Graber ZT, Baumgart T, Stone HA, Cohen AE. Cell Membranes Resist Flow. Cell. 2018;175(7):1769-1779 e1713.

14. Grande-Garcia A, Echarri A, de Rooij J, et al. Caveolin-1 regulates cell polarization and directional migration through Src kinase and Rho GTPases. The Journal of cell biology. 2007;177(4):683-694.

15. Grande-Garcia A, del Pozo MA. Caveolin-1 in cell polarization and directional migration. Eur J Cell Biol. 2008;87(8-9):641-647.

16. Ludwig A, Howard G, Mendoza-Topaz C, et al. Molecular composition and ultrastructure of the caveolar coat complex. PLoS biology. 2013;11(8):e1001640.

eLife assessment

This important study uses convincing time-resolved proximity proteomics, validated with proximity ligation assays, to provide new insight into mechanical regulation of caveolin-1 complexes that form in migrating cells. Solid follow up experiments reveal a reciprocal relationship between mechanosensitive caveolae and RhoGTPase signalling in migrating cells, but evidence supporting a direct link between the newly identified factors with a specific caveolae subpopulation remains incomplete at this stage.

Reviewer #1 (Public Review):

In this study, Girardello et al. use proteomics to reveal the membrane tension sensitive caveolin-1 interactome in migrating cells. The authors use EM and surface rendering to demonstrate that caveolae formed at the rear of migrating cells are complex membrane-linked multilobed structures, and they devise a robust strategy to identify caveolin-1 associated proteins using APEX2-mediated proximity biotinylation. This important dataset is further validated using proximity ligation assays to confirm key interactions, and follows up with an interrogation of a surprising relationship between caveolae and RhoGTPase signalling, where caveolin-1 recruits ROCK1 under high membrane tension conditions, and ROCK1 activity is required to reform caveolae upon reversion to isotonic solution. However, caveolin-1 recruits the RhoA inactivator ARHGAP29 when membrane tension is low and ARHGAP29 overexpression leads to disassembly of caveolae and reduced cell motility. This study builds on previous findings linking caveolae to positive feedback regulation of RhoA signalling, and provides further evidence that caveolae serve to drive rear retraction in migration but also possess an intrinsic brake to limit RhoA activation, leading the authors to suggest that cycles of caveolae assembly and disassembly could thereby be central to establish a stable cell rear for persistent cell migration

A major strength of the manuscript is the robust proteomic dataset. The experimental set up is well defined and mostly well controlled, and there is good internal validation in that the high abundance of core caveolar proteins in low membrane tension (isotonic) conditions, and absence under high membrane tension (brief hypo-osmotic shock) conditions, correlating very well with previous finding. The data could however be better presented to show where statically robust changes occur, and supplementary information should include a table of showing abundance. It's very good to see a link to PRIDE, providing a useful resource for the community.

The authors detail several known interactions and their mechanosensitivty, but also report new interactors of caveolin-1. Several mechanosensitive interactions of caveolin-1 take place at the cell rear, but others are more diffuse across the cell looking at the PLA data (e.g FLN1, CTTN, HSPB1; Figure 4A-F and Figure 4 supplement 1). It is interesting to speculate that those at the cell rear are involved in caveolae, whilst others are linked specifically to caveolin-1 (e.g. dolines). PLA or localisation analysis with Cavin1/PTRF may be able to resolve this and further specify caveolae versus non-caveolae mechanosensitive interactions.

The Cav1/ARHGAP29 influence on YAP signalling is interesting, but appear to be quite isolated from the rest of the manuscript. Does overexpression of ARHGAP29 influence YAP signalling and/or caveolar protein expression/Cav1pY14?<br /> ARHGAP29 and RhoA/ROCK1 related observations are very interesting and potentially really important. However, the link between ARHGAP29 and caveolae is not well established (other than in proteomic data). PLA or FRET could help establish this.<br /> The relationship between ARHGAP29 and RhoA signalling is not well defined. Is GAP activity important in determining the effect on migration and caveolae formation? What is the effect on RhoA activity? Alternatively, the authors could investigate YAP dependent transcriptional regulation downstream of overexpression.

Reviewer #2 (Public Review):

Girardello et al investigated the composition of the molecular machinery of caveolae governing their mechano-regulation in migrating cells. Using live cell imaging and RPE1 cells, the authors provide a spatio-temporal analysis of cavin-3 distribution during cell migration and reveal that caveolae are preferentially localized at the rear of the cell in a stable manner. They further characterize these structures using electron tomography and reveal an organization into clusters connected to the cell surface. By performing a proteomic approach, they address the interactome of caveolin-1 proteins upon mechanical stimulation by exposing RPE1 cells to hypo-osmotic shock (which aims to increase cell membrane tension) or not as a control condition. The authors identify over 300 proteins, notably proteins related to actin cytoskeleton and cell adhesion. These results were further validated in cellulo by interrogating protein-protein interactions using proximity ligation assays and hypo-osmotic shock. These experiments confirmed previous data showing that high membrane tension induces caveolae disassembly in a reversible manner. Eventually, based on literature and on the results collected by the proteomic analysis, authors investigated more deeply the molecular signaling pathway controlling caveolae assembly upon mechanical stimuli. First, they confirm the targeting of ROCK1 with Caveolin-1 and the implication of the kinase activity for caveolae formation (at the rear of the cell). Then, they show that RhoGA ARHGAP29, a factor newly identified by the proteomic analysis, is also implicated in caveolae mechano-regulation likely through YAP protein and found that overexpression of RHoGA ARHGAP29 affects cell motility. Overall, this paper interrogated the role of membrane tension in caveolae located at the rear of the cell and identified a new pathway controlling cell motility.

Strengths:

Using a proximity-based proteomic assay, the authors reveal the protein network interacting with caveolae upon mechanical stimuli. This approach is elegant and allows to identify a substantial new set of factors involved in the mechano-regulation of caveolin-1, some of which have been verified directly in the cell by PLA. This study provides a compelling set of data on the interactions between caveolae and its cortical network which was so far ill-characterized.

Weaknesses:

The methodology demonstrating an impact of membrane tension is not precise enough to directly assess a direct role on caveolae at a subcellular scale, that is between the front and the rear of the cell. First, a better characterization of the "front-rear" cellular model is encouraged. Secondly, authors frequently present osmotic shock as "high membrane tension" stimuli. While osmotic shock is widely used in the field, this study is focused only on caveolae localized at the rear of cell and it remains unclear how the level of a global mechanical stimuli triggered by an osmotic shock could mimic a local stimuli. In the present case, it remains unknown the extent to which this mechanical stress is physiologically relevant to mimic mechanical forces applied at the rear of a migrating cell.<br /> Some images are not satisfying to fully support the conclusions of the article. At this stage, the lack of an unbiased quantitative analysis of the spatio-temporal analysis of caveolae upon well-defined mechanical stimuli is also needed. Cells on images, in particular Figure 1, are difficult to see. Signal-to noise ratio in different cell area could generate a biased. Since there is inconsistency between caveolae density and localization between Figures, more solid illustrations are needed along quantitative analysis.

eLife assessment

This important study defines signaling mechanisms in tendinopathy development, which is significant as there is a clear need to identify therapeutic targets to prevent or reverse tendon pathology. The evidence supporting the conclusions are compelling combining an existing human tendinopathy transcriptomics dataset with ex-vivo assembloid model, and an in vivo injury model using genetic reporter mice. This work will be of interest to developmental and stem cell biologists.

Reviewer #1 (Public Review):

This work by Stauber et al., is focused on understanding the signaling mechanisms that are associated with tendinopathy development, and by screening a panel of human tendinopathy samples, identified IL-6/JAK/STAT as a potential mediator of this pathology. Using an innovate explant model they delineated the requirement for IL-6 in the main body of the tendon to alter the dynamics of extrinsic fibroblasts. These studies are complemented by in vivo studies that include a Scx-GFP reporter. This approach facilitates examination of the effects of IL6-/- on Scx+ cells, and the differences observed between ex vivo and in vivo contexts.

The use of a publicly available existing dataset is considered a strength, since this dataset includes expression data from several different human tendons experiencing tendinopathy. The revised analysis that includes only non-sheathed tendons facilitates the identification of potentially conserved regulators of the tendinopathy phenotype, with immunostaining for CD90, IL-6R, and IL-6 expression in human tendinopathy samples providing important validation of the transcriptomic studies.

Author response:

The following is the authors’ response to the original reviews.

eLife assessment:

This important study details an enrichment of the IL-6 signaling pathway in human tendinopathy and applies transcriptional profiling to an advanced in vitro model to test IL-6 specific phenotypes in tendinopathy. Overall, the strength of evidence is solid yet incomplete, as transcriptomic measurements provide clarity, though functional studies including analysis of proliferation are needed to confirm these findings. This work will be of interest to stem cell biologists and immunologists.

To functionally assess the effect of IL-6 on Scx+ fibroblast proliferation in an acute injury, we repeated the in vivo studies with an EdU staining and a newly established IL-6 KO x ScxGFP+ mouse line. We found no evidence for this effect in acute injuries and acknowledge this in the revised manuscript.

We further added data collected by combining fluorescence microscopy with human patient-derived tissue to strengthen the link between IL-6, IL-6R, and proliferation of CD90+ cells in chronic injuries.

See comment 1.1.

See comment 2.4.

Changes:

- Title

- Abstract

- Figure 2 and 3 (new data)

- Figure 7 (new data)

- Results

- Discussion

Reviewer 1

(1.1) First, the experimental approach does not directly assess proliferation, as such the conclusions regarding proliferation are not well supported. In the ex-vivo model, the use of cell counting approaches is somewhat acceptable since the system is constrained by the absence of potential influx of new cells. However, given the nearly unlimited supply of extrinsically derived cells in vivo (vs. the explant model), assessment of actual proliferation (e.g. Edu, BrdU, Ki67) is critical to support this conclusion.

To assess the effect of IL-6 on Scx+ fibroblast proliferation in an acute injury, we repeated the in vivo studies with an EdU staining and a newly established IL-6 KO x ScxGFP+ mouse line to combat the considerable background noise of currently available Scx antibodies.

Under the improved design of these experiments, we could detect no effect of IL-6 on ScxGFP+ cells in an acute injury in vivo. We have therefore replaced figure 5 with the new results in figure 7 and moved figure 5F to the supplementary materials (Supplementary figure 9).

We acknowledge and discuss this in the discussion section.

See comment 2.4.

See comment 2.11.

Changes:

- Title

- Abstract

- Figure 7 (new data)

- Supplementary Figure 9

- Results

- Discussion

(1.2) Second, the justification for the use of Scx-GFP+ cells as a progenitor population is not well supported. Indeed, in the discussion, Scx+ cells are treated as though they are uniformly a progenitor population, when the diversity of this population has been established by the cited studies, which do not suggest that these are progenitor populations. Additional definition/ delineation of these cells to identify the subset of these cells that may actually display other putative progenitor markers would support the conclusions. As it stands, the study currently provides important information on the impact of IL6 on Scx+ cells, but not tendon progenitors.

We further delineated the extrinsic cell populations isolated from mouse Achilles tendons of ScxGFP+ mice using flow cytometric analysis and RT-qPCR. We used tendon population markers suggested by sc-RNA-seq of mouse Achilles tendons.

(De Micheli et al., Am. J. Physiol. - Cell Physiol., 2020, 319(5), DOI: 10.1152/ajpcell.00372.2020)

While a small subpopulation of these cells expressed typical progenitor markers (i.e. CD45 and CD146), we could detect no overlap with Scx+ cells. As suggested by the reviewer, we therefore replaced occurrences of “progenitor” in the manuscript with “fibroblast” and performed additional experiments with human patient-derived tissue sections and the fibroblast marker CD90.

See comment 2.1.

Changes:

- Title

- Abstract

- Figure 2 (new data)

- Figure 3 (new data)

- Supplementary Figure 6 (new data)

- Results

- Discussion

(1.3) Clarity regarding the relevance of the 'sheath-like' component of the assembloid would provide helpful context regarding which types of tendons are likely to have this type of communication vs. those that do not, and if there are differences in tendinopathy prevalence. Understanding why/how this communication between structures is relevant is important.

Our assembloid concept is inspired by the structure of unsheathed tendons (i.e. biceps, semitendinosus, gracilis) and not sheathed tendons like the flexor tendons.

We agree that clarity regarding the tendon type having this type of communication is important, so we sharpened previously blurry text passages in the revised manuscript.

Text changes:

- Introduction, page 3

- Results, page 4

- Results, page 8

- Results, page 9

- Results, page 11

- Discussion, page 25

- Discussion, page 26

- Experimental section, page 28

- Figure 1

- Figure 2

- Figure 3

- Supplementary Table 1

- Supplementary Figure 3

- Supplementary Figure 4

(1.4) Minor: in the text for Figure 6 (2nd paragraph), the comma in 19,694 is superscripted.

Corrections were made throughout the manuscript.

Text changes:

- Results, page 4

- Results, page 12

- Results, page 19

- Results, page 21

(1.5) Minor: The inclusion of the Scx-GFP mouse should be included in the schematic Figure 5.

The results presented in the previous draft did not feature tissues from ScxGFP mice but used a Scx-antibody to visually detect Scx+ cells. In anticipation of the revision process, we bred a new IL-6 KO x ScxGFP+ mouse line and repeated the experiment. As suggested by the reviewer, the new schematic figure 7 as well as the former figure 5 moved to the supplementary material now includes this mouse.

Figure changes:

- Supplementary Figure 9 (former figure 5)

- Figure 7

Reviewer 2

(2.1) One question that comes to mind is whether the fibroblast progenitors in the extrinsic sheath of Achilles tendon is similar to those surrounding the tail tendon. The similarity of progenitors between different tendons is assumed with this model. I would consider this to be a minor issue.

Tail tendon fascicles are thought to have a low number of reparative fibroblasts / progenitor cells because they lack a developed extrinsic compartment. Achilles tendons are supposed to have a higher number of reparative fibroblasts / progenitor cells, as their fascicles are surrounded by an extrinsic compartment.

To verify this here, we added a better characterization and comparison of the cell populations isolated from the tail tendon fascicles and the Achilles tendons.

First, we added representative light microscopy images of these cells at different timepoints after being cultured on tissue-culture plastic.

Second, we performed flow cytometric analysis not only on the freshly digested tail tendon fascicles and Achilles tendons, but also on the cultured cells at the timepoint when they would have been embedded into the assembloids.

Third, we compared the expression of population-specific markers in cells derived from tail tendon fascicle and Achilles tendons.

As expected, tail tendon fascicle-derived cell populations appeared to be more elongated than Achilles tendon-derived populations shortly after isolation. Similarly, the “maintenance” fibroblasts in healthy tendons are more elongated than the reparative fibroblasts in diseased ones. After culture and priming in tendinopathic niche conditions, both populations assumed a more roundish, reparative phenotype.

This was consistent with the flow cytometric analysis, which revealed a large difference between freshly isolated populations, that disappeared after extended culture and priming in tendinopathic niche conditions. Gene expression in tail tendon fascicle-derived and Achilles tendon-derived cells was similar after extended culture and priming in tendinopathic niche conditions.

See comment 1.2.

See comment 2.10.

Changes:

- Supplementary Figure 6 (new data)

- Results, page 11

(2.2) The authors use core tendons from IL-6 knockout mice and progenitors from wild-type mice. The reasoning behind this approach was a little confusing... is IL-6 expressed solely in the tendon core compared to the extrinsic sheath?

Insights gained from human patient-derived tissues (Figure 2) suggest that in a healthy tendon, most of the IL-6 is located in the extrinsic compartment but distributed over compartments in the tendinopathic ones.

Our assembloid design mimicks this by embedding wildtype fibroblasts into the extrinsic compartment. Our hypothesis was that a wildtype core in tendinopathic niche conditions attracts reparative fibroblasts through IL-6, while an IL-6 knock-out core does not. Therefore, it was important to establish IL-6 gradients close to what they seem to be in vivo.

Nevertheless, we have to acknowledge that the amount of IL-6 secreted by extrinsic fibroblasts in isolation is quite small compared to what is secreted by a wildtype core (Supplementary Figure 7). Attributing IL-6 in the supernatant of a WT core // WT fibroblast assembloid to the correct cell population is challenging but could be part of future research.  

Changes:

- Figure 2 (new data)

- Supplementary Figure 7 (new data)

- Results, page 12

(2.3) Is a co-culture system for 7 days appropriate to model tendinopathy without the supplementation of exogenous inflammatory compounds? The transcriptomic differences in Figure 3 seem to be subtle, and may perhaps suggest that it could be a model that more closely resembles steady state compared to tendinopathy. If so, is IL-6 still relevant during steady state?

The collective experience in our lab is that core explants exposed to tendinopathic niche conditions (i.e. serum, 37°C, high oxygen, and high glucose levels) assume a disease-like phenotype. (i.e. Wunderli et al., Matrix Biology, 2020, Volume 89 https://doi.org/10.1016/j.matbio.2019.12.003 and Blache et al., Sci. Rep., 2021, 11(1), DOI 10.1038/s41598-021-85331-1).

Specifically for our core // fibroblast co-culture system, we have reported the emergence of exaggerated tendinopathic hallmarks in a previous publication (Stauber et al., Adv. Healthc. Mater., 2021, 10(20), https://doi.org/10.1002/adhm.202100741).

We clarified the use of previously validated tendinopathic niche conditions in this manuscript.

Changes:<br /> - Introduction, page 3<br /> - Results, page 12

(2.4) The results presented in Figures 4 and 5 are impressive, demonstrating a link between IL-6 and fibroblast progenitor numbers and migration. Their experimental design in these figures show strong evidence, using Tocilizumab and recombinant IL-6 to rescue shown phenotypes. I would reduce the claims on proliferation, however, unless a proliferation-specific marker (e.g., Ki67, BrdU, EdU) is included in confocal analyses of Scx+ progenitors.

As reviewer 1 pointed out as well, it is important to use a proliferation-specific marker “given the nearly unlimited supply of extrinsically derived cells in vivo (vs. the explant model)”.

To assess the effect of IL-6 on Scx+ fibroblast proliferation in vivo, we repeated those experiments with a proliferation-specific EdU staining and a newly established IL-6 KO x ScxGFP+ mouse line.

Under this improved design, we could not detect an effect of IL-6 on proliferation in an acute injury in vivo.

We have therefore replaced figure 5 with the new results in figure 7 and moved figure 5F to the supplementary materials (Supplementary figure 9).

We acknowledge and discuss this in the discussion section and softened our statements in the title and the abstract.

See comment 1.1.

See comment 2.11.

Changes:

- Title

- Abstract

- Figure 7 (new data)

- Supplementary Figure 9

- Results

- Discussion

(2.5) I think it would significantly strengthen the study if they could measure tendon healing in IL-6 knockouts or in wild-type mice treated with IL-6 inhibitors, since conventional ablation of IL-6 may lead to the elevation of compensatory IL-6 superfamily ligands that could activate STAT signaling. The authors claim that reducing IL-6 signaling decreases transcriptomic signatures of tendinopathy, but IL-6 may be necessary to promote normal healing of the tendon following injury. It is supposed that a lack of Scx+ progenitor migration would delay tendon healing.

Indeed, another study using the same IL-6 knock-out strain showed that a lack of IL-6 signaling resulted in slightly inferior mechanical properties in healing patellar tendons (Lin et al., J. Biomech., 39(1), 2006 https://doi.org/10.1016/j.jbiomech.2004.11.009)

Also, it might be due to the elevation of compensatory IL-6 superfamily ligands that we found no effect of IL-6 on the proliferation of Scx+ cells in an acute injury in vivo.

Therefore, assessing the effects of IL-6 inhibitors on tendon healing following an acute injury would have been of great interest to us. Unfortunately, getting the necessary permission from the animal experimentation office for a new invasive treatment protocol was outside of our scope due to the severity degree and time limitations.

We incorporated and acknowledged these important points in the discussion.

Text changes:

- Introduction, page 3

- Discussion, page 26

(2.6) Do IL-6 knockout mice and/or mice treated with IL-6 inhibitors have delayed healing following Achilles tendon resection? Please provide experimental evidence.

See comment 2.5.

(2.7) I would suggest reducing claims on proliferation, or include a proliferation specific marker (e.g., Ki67, BrdU, EdU) in confocal analyses of Scx+ progenitors.

See comment 1.1.

See comment 2.4.

(2.8) Supplementary Figures 1 and 2: the authors removed outliers. Please specify exactly which outliers were removed in the figures, and provide additional information on the criteria used to identify these outliers.

To address this comment, we sharpened our criteria for identifying outliers and re-did the analysis depicted in figure 1.

Briefly, we excluded 5 normal and 5 tendinopathic samples from sheathed tendons which have a different compartmental structure than unsheathed tendons.

A complete separate analysis of the sheathed tendons would have been beyond the scope of this manuscript, but early screening suggested that IL-6 transcripts are not increased in sheathed tendinopathic tendons.

We made text changes throughout the manuscript and to the supplementary table 1 and supplementary figure 2 to clearly state our criteria for excluding samples / outliers.

Changes:

- Introduction, page 3

- Results, page 4

- Results, page 8

- Results, page 9

- Results, page 11

- Discussion, page 25

- Discussion, page 26

- Experimental section, page 28

- Figure 1,

- Figure 2,

- Figure 3,

- Supplementary table 1,

- Supplementary figure 2,

- Supplementary figure 3,

- Supplementary figure 4,

(2.9) Whenever "positive enrichment" is mentioned in the text, please specify in what group. It is presumed that the enrichment, for example, in the first figure is associated with tendinopathy samples compared to controls, though it is a bit unclear.

The direction of the enrichment was added to the text.

Text changes:

- Abstract, page 1

- Introduction, page 3

- Results, page 4

- Results, page 6

- Results, page 12

- Results, page 14

- Results, page 19

- Results, page 21

- Discussion, page 25

- Discussion, page 26

- Discussion, page 27

- Figure 1

- Figure 5

- Figure 8

- Figure 9

- Supplementary figure 3

- Supplementary figure 4

- Supplementary figure 6

- Supplementary figure 8

- Supplementary figure 11

- Supplementary figure 12

- Supplementary figure 14

(2.10) Are tail tendon progenitors similar to Achilles tendon progenitors? Please provide a statement that shows similarity (in function, transcriptome, etc.) to support the in vitro tendon model.

See comment 1.2.

See comment 2.1.

(2.11) Are the results in Figure 5F significant? It seems that your pictures show a dramatic change in migration, but the quantification does not?

We repeated the in vivo studies with a newly established IL-6 KO x ScxGFP+ mouse line to combat the considerable background noise of currently available Scx antibodies.

Under the improved design of these experiments, we could not detect an effect of IL-6 on ScxGFP+ cells migration in an acute injury in vivo.

We have therefore replaced figure 5 with the new results in figure 7 and moved figure 5F to the supplementary materials (Supplementary figure 9)

We acknowledge and discuss this in the discussion section.

See comment 1.1.

See comment 2.4.

Changes:

- Title

- Abstract

- Figure 7 (new data)

- Supplementary Figure 9

- Results

- Discussion

(2.12) Please provide additional discussion points on cis- versus trans-IL6 signaling in your results found in mouse. Do you think researchers/clinicians would want to target trans-IL6 signaling based on your results? Please support these statements with the expression of IL6R on cells found in the tendon core and external sheath progenitors.

To address this comment, we performed flow cytometric analysis on Achilles tendon-derived fibroblasts expanded in 2D and digested sub-compartments of the assembloids (Supplementary Figure 7).

These data suggest that IL6R is neither expressed by core nor extrinsic fibroblasts, but mainly comes from core-resident CD45+ tenophages.

Human samples co-stained for IL6R and CD68 (an established human macrophage marker) confirmed macrophages as a source of IL-6R in vivo. However, human samples co-stained for IL6R and CD90 (an established marker of reparative fibroblasts in humans) also detected IL6R on CD90+ cells, which have not yet been reported to express IL6R themselves.

Overall, it is likely that trans-IL-6 signaling is more important for the activation of reparative fibroblasts than cis-IL-6 signaling. We added these statements to the manuscript.

Changes:

- Results, page 9

- Results, page 12

- Discussion, page 25

- Discussion, page 26

- Figure 3 (new data)

- Supplementary figure 7 (new data)

(2.13) Please provide more detail on collagen isolation from rat tail in the methods section.

We provided more details on collagen isolation from rat tail in the experimental section (page 29)

Changes:

- Experimental section, page 29

(2.14) Please comment on whether your in vitro system resembles tendinopathy or a steady state tendon. If it models more of a steady state system, would IL-6 still be relevant?

See comment 2.3.

Detailed feedback:

Reviewer 1:

This work by Stauber et al. is focused on understanding the signaling mechanisms that are associated with tendinopathy development, and by screening a panel of human tendinopathy samples, identified IL-6/JAK/STAT as a potential mediator of this pathology. Using an innovative explant model they delineated the requirement for IL-6 in the main body of the tendon to alter the dynamics of cells in the peritendinous synovial sheath space.

The use of a publicly available existing dataset is considered a strength since this dataset includes expression data from several different human tendons experiencing tendinopathy. This facilitates the identification of potentially conserved regulators of the tendinopathy phenotype.

The clear transcriptional shifts between WT and IL6-/- cores demonstrates the utility of the assembloid model, and supports the importance of IL6 in potentiating the cell response to this stimuli.

Reviewer 2:

The authors of this study describe a goal of elucidating the signaling pathways that are upregulated in tendinopathy in order to target these pathways for effective treatments. Their goal is honorable, as tendinopathy is a common debilitating condition with limited treatments. The authors find that IL-6 signaling is upregulated in human tendinopathy samples with transcriptomic and GSEA analyses. The evidence of their initial findings are strong, providing a clinically-relevant phenotype that can be further studied using animal models.

Along these lines, the authors continue with an advanced in vitro system using the mouse tail tendon as the core with progenitors isolated from the Achilles tendon as the external sheath embedded in a hydrogel matrix. One question that comes to mind is whether the fibroblast progenitors in the extrinsic sheath of Achilles tendon is similar to those surrounding the tail tendon. The similarity of progenitors between different tendons is assumed with this model. I would consider this to be a minor issue, and would consider the in vitro system to be an additional strength of this study.

In order to address the IL-6 signaling pathway, the authors use core tendons from IL-6 knockout mice and progenitors from wild-type mice. The reasoning behind this approach was a little confusing... is IL-6 expressed solely in the tendon core compared to the extrinsic sheath? Furthermore, is a co-culture system for 7 days appropriate to model tendinopathy without the supplementation of exogenous inflammatory compounds? The transcriptomic differences in Figure 3 seem to be subtle, and may perhaps suggest that it could be a model that more closely resembles steady state compared to tendinopathy. If so, is IL-6 still relevant during steady state?

Nevertheless, the results presented in Figures 4 and 5 are impressive, demonstrating a link between IL-6 and fibroblast progenitor numbers and migration. Their experimental design in these figures show strong evidence, using Tocilizumab and recombinant IL-6 to rescue shown phenotypes. I would reduce the claims on proliferation, however, unless a proliferation-specific marker (e.g., Ki67, BrdU, EdU) is included in confocal analyses of Scx+ progenitors. The Achilles tendon injury model provides a nice in vivo confirmation of Scx-progenitor migration to the neotendon.

Given their goal to elucidate signaling pathways that could be targeted in the clinic, I think it would significantly strengthen the study if they could measure tendon healing in IL-6 knockouts or in wild-type mice treated with IL-6 inhibitors, since conventional ablation of IL-6 may lead to the elevation of compensatory IL-6 superfamily ligands that could activate STAT signaling. The authors claim that reducing IL-6 signaling decreases transcriptomic signatures of tendinopathy, but IL-6 may be necessary to promote normal healing of the tendon following injury. It is supposed that a lack of Scx+ progenitor migration would delay tendon healing.

Overall, the authors of this study elucidated IL-6 signaling in tendinopathy and provided a strong level of evidence to support their conclusions at the transcriptomic level. However, functional studies are needed to confirm these phenotypes and fully support their aims and conclusions. With these additional studies, this work has the potential to significantly influence treatments for those suffering from tendinopathy.

Reviewer #1 (Public Review):

The manuscript by Wang et al is, like its companion paper, very unusual in the opinion of this reviewer. It builds off of the companion theory paper's exploration of the "Wright-Fisher Haldane" model but applies it to the specific problem of diversity in ribosomal RNA arrays. The authors argue that polymorphism and divergence among rRNA arrays are inconsistent with neutral evolution, primarily stating that the amount of polymorphism suggests a high effective size and thus a slow fixation rate, while we, in fact, observe relatively fast fixation between species, even in putatively non-functional regions. They frame this as a paradox in need of solving, and invoke the WFH model.

The same critiques apply to this paper as to the presentation of the WFH model and the lack of engagement with the literature, particularly concerning Cannings models and non-diffusive limits. However, I have additional concerns about this manuscript, which I found particularly difficult to follow.

My first, and most major, concern is that I can never tell when the authors are referring to diversity in a single copy of an rRNA gene compared to when they are discussing diversity across the entire array of rRNA genes. I admit that I am not at all an expert in studies of rRNA diversity, so perhaps this is a standard understanding in the field, but in order for this manuscript to be read and understood by a larger number of people, these issues must be clarified.

The authors frame the number of rRNA genes as roughly equivalent to expanding the population size, but this seems to be wrong: the way that a mutation can spread among rRNA gene copies is fundamentally different than how mutations spread within a single copy gene. In particular, a mutation in a single copy gene can spread through vertical transmission, but a mutation spreading from one copy to another is fundamentally horizontal: it has to occur because some molecular mechanism, such as slippage, gene conversion, or recombination resulted in its spread to another copy. Moreover, by collapsing diversity across genes in an rRNA array, the authors are massively increasing the mutational target size.

For example, it's difficult for me to tell if the discussion of heterozygosity at rRNA genes in mice starting on line 277 is collapsed or not. The authors point out that Hs per kb is ~5x larger in rRNA than the rest of the genome, but I can't tell based on the authors' description if this is diversity per single copy locus or after collapsing loci together. If it's the first one, I have concerns about diversity estimation in highly repetitive regions that would need to be addressed, and if it's the second one, an elevated rate of polymorphism is not surprising, because the mutational target size is in fact significantly larger.

Even if these issues were sorted out, I'm not sure that the authors framing, in terms of variance in reproductive success is a useful way to understand what is going on in rRNA arrays. The authors explicitly highlight homogenizing forces such as gene conversion and replication slippage but then seem to just want to incorporate those as accounting for variance in reproductive success. However, don't we usually want to dissect these things in terms of their underlying mechanism? Why build a model based on variance in reproductive success when you could instead explicitly model these homogenizing processes? That seems more informative about the mechanism, and it would also serve significantly better as a null model, since the parameters would be able to be related to in vitro or in vivo measurements of the rates of slippage, gene conversion, etc.

In the end, I find the paper in its current state somewhat difficult to review in more detail, because I have a hard time understanding some of the more technical aspects of the manuscript while so confused about high-level features of the manuscript. I think that a revision would need to be substantially clarified in the ways I highlighted above.

Author response:

(1) First, we wish to point out that there has not been a model for quantifying genetic drift in multi-copy gene systems.  Hence, the first attempt using the Haldane model is not expected to be familiar and readily acceptable. Nevertheless, the standard WF (Wright-Fisher) model cannot handle drift in multi-copy gene systems, such as viruses, due to the two levels of genetic drift – within individuals as well as between individuals of the population.

[Point 1 responds to the comments that we did not engage with the literature, in particular, publications like the Canning model, which are extensions of the WF model. As pointed out above, models based on the WF sampling cannot handle the two levels of genetic drift.]

(2) A crucial aspect of the study is the nature of rRNA gene cluster, which is also a multi-copy gene system. It is easy to see some multi-copy gene systems, like viral particles or mtDNAs, to have a sub-population of genes within each individual. It is less obvious that tandem arrays of gene copies like rRNA genes can be treated as sub-populations that are subjected to drift. Nevertheless, rRNA gene copies frequently transfer mutations among copies in the same cell via the homogenization process. Hence, rRNA genes do not have the property of "locus" of single-copy genes as they move about as well (a bit like transposons but via different mechanisms). Indeed, the collection of rRNA genes in a cell is referred to as the “community of genes” as cited in Fig. 1. Over hundreds of generations, rRNA genes are effectively a small gene pool like mtDNAs within cells.  Furthermore, the copy number of rRNA genes also changes rapidly among individuals. For these reasons, genetic drift is operative within cells and this study aims to determine its strength (see Response 3 below).

[Point 2 of the response addresses questions of Review #1 such as "(whether) the authors are referring to diversity in a single copy of an rRNA gene (or) diversity across the entire array of rRNA genes" or "(whether) the discussion of heterozygosity at rRNA ... is diversity per single copy locus or after collapsing loci together". The answer should be "the genetic diversity of the population of rRNA genes in the cell", noting that the single gene locus does not apply here. Similarly, a question like "Alignment to a single reference genome would likely lead to incorrect and even failed alignment for some reads'" from Review #2 appears to be based on the homology concept of a rRNA gene locus.  All rRNA gene copies are aligned against the consensus of the population of genes of the species. The consensus nucleotide nearly always accounts for > 90% of the gene copies in the population.]

(3) We now clarify the meaning of C*, the effective copy number of rRNA genes. We apologize that the abstract is indeed unclear, and even misleading. In the abstract, we did not use different notations for the actual copy number (C) and the effective copy number (C*) of rRNA genes. Instead, we use the letter C to designate both.  Furthermore, in the main text, the presentation of the effective number, C*, is overly complicated (in order to be realistic).  We apologize. Slight modifications of the abstract should have removed all the mis-understandings, as shown below.

"On average, rDNAs have C ~ 150 - 300 copies per haploid in humans. While a neutral mutation of a single-copy gene would take 4N (N being the population size) generations to become fixed, the time should be 4NC generations for rRNA genes where 1<< C (C being the effective copy number; C > C or C <C will depend on the strength of drift). However, the observed fixation time in mouse and human is < 4N, implying the paradox of C < 1. Genetic drift that encompasses all random neutral evolutionary forces appears as much as 100 times stronger for rRNA genes as for single-copy genes, thus reducing C* to < 1."

[Point 3 responds to the key criticisms.  From Review #1 " The authors frame the number of rRNA genes as roughly equivalent to expanding the population size, ... a mutation can spread among rRNA gene copies is fundamentally different   …". Indeed, the abstract can be very misleading when it uses CN interchangeably with C*N, essentially by allowing C to mean both. 

From Review #2 "In Eq (1), although C is defined as the "effective copy number", it is unclear what it means in an empirical sense…".  From the slightly revised text quoted above, it should be clear that the fixation time as well as the level of polymorphism represent the empirical measures of C".

(4) Lastly, we shall address the mis-understood "reproductive success" of rRNA genes, which is the number of progeny, K, in the Haldane model. K should be more accurately referred to as the transmission speed. For single-copy genes, reproductive success and transmission both mean the same thing, K. But the term reproductive success is not appropriate for rRNA genes even though the formulae for K are the same for all gene systems

[Point 4 responds to all criticisms using the term "reproductive success"]

eLife assessment

This study attempts to resolve an apparent paradox of rapid evolutionary rates of multi-copy gene systems by using a theoretical model that integrates two classic population models. While the conceptual framework is intuitive and thus useful, the specific model is perplexing and difficult to penetrate for non-specialists. The data analysis of rRNA genes provides inadequate support for the conclusions due to a lack of consideration of technical challenges, mutation rate variation, and the relationship between molecular processes and model parameters.

Reviewer #2 (Public Review):

Summary:

Multi-copy gene systems are expected to evolve slower than single-copy gene systems because it takes longer for genetic variants to fix in the large number of gene copies in the entire population. Paradoxically, their evolution is often observed to be surprisingly fast. To explain this paradox, the authors hypothesize that the rapid evolution of multi-copy gene systems arises from stronger genetic drift driven by homogenizing forces within individuals, such as gene conversion, unequal crossover, and replication slippage. They formulate this idea by combining the advantages of two classic population genetic models -- adding the V(k) term (which is the variance in reproductive success) in the Haldane model to the Wright-Fisher model. Using this model, the authors derived the strength of genetic drift (i.e., reciprocal of the effective population size, Ne) for the multi-copy gene system and compared it to that of the single-copy system. The theory was then applied to empirical genetic polymorphism and divergence data in rodents and great apes, relying on comparison between rRNA genes and genome-wide patterns (which mostly are single-copy genes). Based on this analysis, the authors concluded that neutral genetic drift could explain the rRNA diversity and evolution patterns in mice but not in humans and chimpanzees, pointing to a positive selection of rRNA variants in great apes.

Strengths:

Overall, the new WFH model is an interesting idea. It is intuitive, efficient, and versatile in various scenarios, including the multi-copy gene system and other cases discussed in the companion paper by Ruan et al.

Weaknesses:

Despite being intuitive at a high level, the model is a little unclear, as several terms in the main text were not clearly defined and connections between model parameters and biological mechanisms are missing. Most importantly, the data analysis of rRNA genes is extremely over-simplified and does not adequately consider biological and technical factors that are not discussed in the model. Even if these factors are ignored, the authors' interpretation of several observations is unconvincing, as alternative scenarios can lead to similar patterns. Consequently, the conclusions regarding rRNA genes are poorly supported. Overall, I think this paper shines more in the model than the data analysis, and the modeling part would be better presented as a section of the companion theory paper rather than a stand-alone paper. My specific concerns are outlined below.

(1) Unclear definition of terms

Many of the terms in the model or the main text were not clearly defined the first time they occurred, which hindered understanding of the model and observations reported. To name a few:

(i) In Eq(1), although C* is defined as the "effective copy number", it is unclear what it means in an empirical sense. For example, Ne could be interpreted as "an ideal WF population with this size would have the same level of genetic diversity as the population of interest" or "the reciprocal of strength of allele frequency change in a unit of time". A few factors were provided that could affect C*, but specifically, how do these factors impact C*? For example, does increased replication slippage increase or decrease C*? How about gene conversion or unequal cross-over? If we don't even have a qualitative understanding of how these processes influence C*, it is very hard to make interpretations based on inferred C*. How to interpret the claim on lines 240-241 (If the homogenization is powerful enough, rRNA genes would have C*<1)? Please also clarify what C* would be, in a single-copy gene system in diploid species.

(ii) In Eq(1), what exactly is V*(K)? Variance in reproductive success across all gene copies in the population? What factors affect V*(K)? For the same population, what is the possible range of V*(K)/V(K)? Is it somewhat bounded because of biological constraints? Are V*(K) and C*(K) independent parameters, or does one affect the other, or are both affected by an overlapping set of factors?

(iii) In the multi-copy gene system, how is fixation defined? A variant found at the same position in all copies of the rRNA genes in the entire population?

(iv) Lines 199-201, HI, Hs, and HT are not defined in the context of a multi-copy gene system. What are the empirical estimators?

(v) Line 392-393, f and g are not clearly defined. What does "the proportion of AT-to-GC conversion" mean? What are the numerator and denominator of the fraction, respectively?

(2) Technical concerns with rRNA gene data quality

Given the highly repetitive nature and rapid evolution of rRNA genes, myriads of things could go wrong with read alignment and variant calling, raising great concerns regarding the data quality. The data source and methods used for calling variants were insufficiently described at places, further exacerbating the concern.

(i) What are the accession numbers or sample IDs of the high-coverage WGS data of humans, chimpanzees, and gorillas from NCBI? How many individuals are in each species? These details are necessary to ensure reproducibility and correct interpretation of the results.

(ii) Sequencing reads from great apes and mice were mapped against the human and mouse rDNA reference sequences, respectively (lines 485-486). Given the rapid evolution of rRNA genes, even individuals within the same species differ in copy number and sequences of these genes. Alignment to a single reference genome would likely lead to incorrect and even failed alignment for some reads, resulting in genotyping errors. Differences in rDNA sequence, copy number, and structure are even greater between species, potentially leading to higher error rates in the called variants. Yet the authors provided no justification for the practice of aligning reads from multiple species to a single reference genome nor evidence that misalignment and incorrect variant calling are not major concerns for the downstream analysis.

(vi) It is unclear how variant frequency within an individual was defined conceptually or computed from data (lines 499-501). The population-level variant frequency was calculated by averaging across individuals, but why was the averaging not weighted by the copy number of rRNA genes each individual carries? How many individuals are sampled for each species? Are the sample sizes sufficient to provide an accurate estimate of population frequencies?

(vii) Fixed variants are operationally defined as those with a frequency>0.8 in one species. What is the justification for this choice of threshold? Without knowing the exact sample size of the various species, it's difficult to assess whether this threshold is appropriate.

(viii) It is not explained exactly how FIS, FST, and divergence levels of rRNA genes were calculated from variant frequency at individual and species levels. Formulae need to be provided to explain the computation.

(3) Complete ignorance of the difference in mutation rate difference between rRNA genes and genome-wide average

Nearly all data analysis in this paper relied on comparison between rRNA genes with the rest (presumably single-copy part) of the genome. However, mutation rate, a key parameter determining the diversity and divergence levels, was completely ignored in the comparison. It is well known that mutation rate differs tremendously along the genome, with both fine and large-scale variation. If the mutation rate of rRNA genes differs substantially from the genome average, it would invalidate almost all of the analysis results. Yet no discussion or justification was provided.

Related to mutation rate: given the hypermutability of CpG sites, it is surprising that the evolution/fixation rate of rRNA estimated with or without CpG sites is so close (2.24% vs 2.27%). Given the 10 - 20-fold higher mutation rate at CpG sites in the human genome, and 2% CpG density (which is probably an under-estimate for rDNA), we expect the former to be at least 20% higher than the latter.

Among the weaknesses above, concern (1) can be addressed with clarification, but concerns (2) and (3) invalidate almost all findings from the data analysis and cannot be easily alleviated with a complete revamp work.

eLife assessment

This important study by Lee and colleagues examined how neural representations are transformed between the olfactory tubercle (OT) and the ventral pallidum (VP) using single neuron calcium imaging in head-fixed mice trained in classical conditioning. They show that the dimensionality of neural responses is lower in the VP than in the OT and suggest that VP responses represent values in a more abstract form at the single neuron level while OT contains more odor information, potentially enhancing odor contrast. The results are overall convincing and this study provides insights into how odor information is transformed in the olfactory system.

Reviewer #1 (Public Review):

In this manuscript, Lee et al. compared encoding of odor identity and value by calcium signaling from neurons in the ventral pallidum (VP) in comparison to D1 and D2 neurons in the olfactory tubercle (OT).

Strengths:

They utilize a strong comparative approach, which allows the comparison of signals in two directly connected regions. First, they demonstrate that both D1 and D2 OT neurons project strongly to the VP, but not the VTA or other examined regions, in contrast to accumbal D1 neurons which project strongly to the VTA as well as the VP. They examine single unit calcium activity in a robust olfactory cue conditioning paradigm that allows them to differentiate encoding of olfactory identity versus value, by incorporating two different sucrose, neutral and air puff cues with different chemical characteristics. They then use multiple analytical approaches to demonstrate strong, low-dimensional encoding of cue value in the VP, and more robust, high-dimensional encoding of odor identity by both D1 and D2 OT neurons, though D1 OT neurons are still somewhat modulated by reward contingency/value. Finally, they utilize a modified conditioning paradigm that dissociates reward probability and lick vigor to demonstrate that VP encoding of cue value is not dependent on encoding of lick vigor during sucrose cues, and that separable populations of VP neuros encode cue value/sucrose probability and lick vigor. Direct comparisons of single unit responses between the two regions now utilize linear mixed effects models with random effects for subject,

Weaknesses:

The manuscript still includes mention of differences in effect size or differing "levels" of significance between VP and OT D1 neurons without reports of a direct comparisons between the two populations. This is somewhat mitigated by the comprehensive statistical reporting in the supplemental information, but interpretation of some of these results is clouded by the inclusion of OT D2 neurons in these analyses, and the limited description or contextualization in the main text.

Reviewer #2 (Public Review):

We appreciate the authors revision of this manuscript and toning down some of the statements regarding "contradictory" results. We still have some concerns about the major claims of this paper which lead us to suggest this paper undergo more revision as follows since, in its present form, we fear this paper is misleading for the field in two areas. here is a brief outline:

(1) Despite acknowledging that the injections only occurred in the anteromedial aspect of the tubercle, the authors still assert broad conclusions regarding where the tubercle projects and what the tubercle does. for instance, even the abstract states "both D1 and D2 neurons of the OT project primarily to the VP and minimally elsewhere" without mention that this is the "anteromedial OT". Every conclusion needs to specify this is stemming from evidence in just the anteromedial tubercle, as the authors do in some parts of the the discussion.

(2) The authors now frame the 2P imaging data that D1 neuron activity reflects "increased contrast of identity or an intermediate and multiplexed encoding of valence and identity". I struggle to understand what the authors are actually concluding here. Later in discussion, the authors state that they saw that OT D1 and D2 neurons "encode odor valence" (line 510). We appreciate the authors note that there is "poor standardization" when it comes to defining valence (line 521). We are ok with the authors speculating and think this revision is more forthcoming regarding the results and better caveats the conclusions. I suggest in abstract the authors adjust line 14/15 to conclude that, "While D1 OT neurons showed larger responses to rewarded odors, in line with prior work, we propose this might be interpreted as identity encoding with enhanced contrast." [eliminating "rather than valence encoding" since that is a speculation best reserved for discussion as the authors nicely do.

The above items stated, one issue comes to mind, and that is, why of all reasons would the authors find that the anteromedial aspect of the tubercle is not greatly reflecting valence. the anteromedial aspect of the tubercle, over all other aspects of the tubercle, is thought my many to more greatly partake in valence and other hedonic-driven behaviors given its dense reception of VTA DAergic fibers (as shown by Ikemoto, Kelsch, Zhang, and others). So this finding is paradoxical in contrast to if the authors would had studied the anterolateral tubercle or posterior lateral tubercle which gets less DA input.

Reviewer #3 (Public Review):

Summary:

This manuscript describes a study of the olfactory tubercle in the context of reward representation in the brain. The authors do so by studying the responses of OT neurons to odors with various reward contingencies and compare systematically to the ventral pallidum. Through careful tracing, they present convincing anatomical evidence that the projection from the olfactory tubercle is restricted to the lateral portion of the ventral pallidum.

Using a clever behavioral paradigm, the authors then investigate how D1 receptor- vs. D2 receptor-expressing neurons of the OT respond to odors as mice learn different contingencies. The authors find that, while the D1-expressing OT neurons are modulated marginally more by the rewarded odor than the D2-expressing OT neurons as mice learn the contingencies, this modulation is significantly less than is observed for the ventral pallidum. In addition, neither of the OT neuron classes shows conspicuous amount of modulation by the reward itself. In contrast, the OT neurons contained information that could distinguish odor identities. These observations have led the authors to conclude that the primary feature represented in the OT may not be reward.

Strengths:

The highly localized projection pattern from olfactory tubercle to ventral pallidum is a valuable finding and suggests that studying this connection may give unique insights into the transformation of odor by reward association.

Comparison of olfactory tubervle vs. ventral pallidum is a good strategy to further clarify the olfactory tubercle's position in value representation in the brain.

Weaknesses:

The study comes to a different conclusion about the olfactory tubercle regarding reward representations from several other prior works. Whether this stems from a difference in the experimental configurations such as behavioral paradigms used or indeed points to a conceptually different role for the olfactory tubercle remains to be seen.

Author response:

The following is the authors’ response to the previous reviews.

Public Reviews:

Reviewer #1 (Public Review):

In this manuscript, Lee et al. compared encoding of odor identity and value by calcium signaling from neurons in the ventral pallidum (VP) in comparison to D1 and D2 neurons in the olfactory tubercle (OT).

Strengths:

They utilize a strong comparative approach, which allows the comparison of signals in two directly connected regions. First, they demonstrate that both D1 and D2 OT neurons project strongly to the VP, but not the VTA or other examined regions, in contrast to accumbal D1 neurons which project strongly to the VTA as well as the VP. They examine single unit calcium activity in a robust olfactory cue conditioning paradigm that allows them to differentiate encoding of olfactory identity versus value, by incorporating two different sucrose, neutral and air puff cues with different chemical characteristics. They then use multiple analytical approaches to demonstrate strong, low-dimensional encoding of cue value in the VP, and more robust, high-dimensional encoding of odor identity by both D1 and D2 OT neurons, though D1 OT neurons are still somewhat modulated by reward contingency/value. Finally, they utilize a modified conditioning paradigm that dissociates reward probability and lick vigor to demonstrate that VP encoding of cue value is not dependent on encoding of lick vigor during sucrose cues, and that separable populations of VP neuros encode cue value/sucrose probability and lick vigor. Direct comparisons of single unit responses between the two regions now utilize linear mixed effects models with random effects for subject,

Weaknesses:

The manuscript still includes mention of differences in effect size or differing "levels" of significance between VP and OT D1 neurons without reports of a direct comparisons between the two populations. This is somewhat mitigated by the comprehensive statistical reporting in the supplemental information, but interpretation of some of these results is clouded by the inclusion of OT D2 neurons in these analyses, and the limited description or contextualization in the main text.

We think the reviewer is mistaken and have clarified the text.  Each pairwise comparison between VP, OTD1 and OTD2, for each odor across days is shown as a heatmap in supplementary figure 8B, with further details in table 37. Absolute diff 3H no statistics

Reviewer #2 (Public Review):

We appreciate the authors revision of this manuscript and toning down some of the statements regarding "contradictory" results. We still have some concerns about the major claims of this paper which lead us to suggest this paper undergo more revision as follows since, in its present form, we fear this paper is misleading for the field in two areas. here is a brief outline:

(1) Despite acknowledging that the injections only occurred in the anteromedial aspect of the tubercle, the authors still assert broad conclusions regarding where the tubercle projects and what the tubercle does. for instance, even the abstract states "both D1 and D2 neurons of the OT project primarily to the VP and minimally elsewhere" without mention that this is the "anteromedial OT". Every conclusion needs to specify this is stemming from evidence in just the anteromedial tubercle, as the authors do in some parts of the the discussion.

We have clarified in multiple locations that we are recorded from the anteromedial OT, including the abstract, and further clarified this in the conclusions throughout the results and discussion. We refrain stating “anteromedial OT” at every mention of the OT, but think we have now made it abundantly clear that our observations are from the anteromedial OT. It is worth noting that retrograde tracing from the VTA did not label any neuron in any part of the OT, suggesting that the conclusion may well extend beyond the anteromedial portion. Though, we acknowledge further work is needed to comprehensively characterize the OT outputs.

(2) The authors now frame the 2P imaging data that D1 neuron activity reflects "increased contrast of identity or an intermediate and multiplexed encoding of valence and identity". I struggle to understand what the authors are actually concluding here. Later in discussion, the authors state that they saw that OT D1 and D2 neurons "encode odor valence" (line 510). 

The point we aim to make is that valence encoding is different between the OT and VP. We do not think the reward modulated activity in OT is valence encoding, at least not as it is in the VP.  We do observe some valence encoding at the population level, which is different from individual valence encoding neurons. The ability of classifiers to segregate population activity based on reward might be considered valence encoding, but we contrast it with that in VP where individual neurons signal reward prediction. This is more robust than that in the OT data where few neurons robustly encode valence. The increased response of the OTD1 neurons after reward association, is more consistent with contrast enhancement than valence encoding.  We believe this distinction is important and reflects a transformation between two reward-related brain areas. For clarification of the sentence in question we have changed it to reflects “increased contrast of iden-ty or an intermediate encoding of valence that also encodes iden-ty.” (line 488)

We appreciate the authors note that there is "poor standardization" when it comes to defining valence (line 521). We are ok with the authors speculating and think this revision is more forthcoming regarding the results and better caveats the conclusions. I suggest in abstract the authors adjust line 14/15 to conclude that, "While D1 OT neurons showed larger responses to rewarded odors, in line with prior work, we propose this might be interpreted as identity encoding with enhanced contrast." [eliminating "rather than valence encoding" since that is a speculation best reserved for discussion as the authors nicely do.

We accept this suggestion and have modified the abstract sentence to say, “Though D1 OT neurons showed larger responses to rewarded odors than other odors, consistent with prior findings, we interpret this as iden-ty encoding with enhanced contrast.”  We believe this is appropriately qualified as an interpreta-on, and should not be confusing.

The above items stated, one issue comes to mind, and that is, why of all reasons would the authors find that the anteromedial aspect of the tubercle is not greatly reflecting valence. the anteromedial aspect of the tubercle, over all other aspects of the tubercle, is thought my many to more greatly partake in valence and other hedonic-driven behaviors given its dense reception of VTA DAergic fibers (as shown by Ikemoto, Kelsch, Zhang, and others). So this finding is paradoxical in contrast to if the authors would had studied the anterolateral tubercle or posterior lateral tubercle which gets less DA input.

We agree that this seems surprising.  This is why we focused on the anteromedial expecting to find valence encoding.  It remains possible that other parts of the OT, or more dorsal aspects of the anteromedial OT encode valence, as has been reported by Murthy and colleagues.  However, it remains unclear if their recordings are in the OT or VP.  Nonetheless our findings indicate that more work is required to understand the contribution of the OT to valence encoding.  It is also important to note that our conclusions are drawn in comparison to the VP, which has more robust valence encoding than the OT. Thus, in comparison the OT sample in our recordings lack robust valence signaling.  We think this comparison is important, due to the lack of clear framework for defining valence that may create misleading statements in past OT work.  

Reviewer #3 (Public Review):

Summary:

This manuscript describes a study of the olfactory tubercle in the context of reward representation in the brain. The authors do so by studying the responses of OT neurons to odors with various reward contingencies and compare systematically to the ventral pallidum. Through careful tracing, they present convincing anatomical evidence that the projection from the olfactory tubercle is restricted to the lateral portion of the ventral pallidum.

Using a clever behavioral paradigm, the authors then investigate how D1 receptor- vs. D2 receptor-expressing neurons of the OT respond to odors as mice learn different contingencies. The authors find that, while the D1-expressing OT neurons are modulated marginally more by the rewarded odor than the D2-expressing OT neurons as mice learn the contingencies, this modulation is significantly less than is observed for the ventral pallidum. In addition, neither of the OT neuron classes shows conspicuous amount of modulation by the reward itself. In contrast, the OT neurons contained information that could distinguish odor identities. These observations have led the authors to conclude that the primary feature represented in the OT may not be reward.

Strengths:

The highly localized projection pattern from olfactory tubercle to ventral pallidum is a valuable finding and suggests that studying this connection may give unique insights into the transformation of odor by reward association.

Comparison of olfactory tubervle vs. ventral pallidum is a good strategy to further clarify the olfactory tubercle's position in value representation in the brain.

Weaknesses:

The study comes to a different conclusion about the olfactory tubercle regarding reward representations from several other prior works. Whether this stems from a difference in the experimental configurations such as behavioral paradigms used or indeed points to a conceptually different role for the olfactory tubercle remains to be seen.

We acknowledge that our results lead us to conclusions that are different from that of prior work.  But we note that our results are not directly at odds, as we see similar reward modulation of D1 OT neurons as has been reported previously. Our conclusion is different because we contrast our OT responses with that in the VP where valence is more robustly encoded at the single neuron level. We also note, that many of the past studies do not define valence as stringently as we do.  Thus, increased activity with reward, as observed in our data and past studies, seems more like reward modulation than valence.

Reviewer #1 (Public Review):

Summary:

This work explored intra and interspecific niche partitioning along spatial, temporal, and dietary niche partitioning between apex carnivores and mesocarnivores in the Qilian Mountain National Park of China, using camera trapping data and DNA metabarcoding sequencing data. They conclude that spatial niche partitioning plays a key role in facilitating the coexistence of apex carnivore species, spatial and temporal niche partitioning facilitate the coexistence of mesocarnivore species, and spatial and dietary niche partitioning facilitate the coexistence between apex and mesocarnivore species. The information presented in this study is important for wildlife conservation and will contribute substantially to the current understanding of carnivore guilds and effective conservation management in fragile alpine ecosystems.

Strengths:

Extensive fieldwork is evident in the study. Aiming to cover a large percentage of the Qilian Mountain National Park, the study area was subdivided into squares, as a geographical reference to distribute the sampling points where the camera traps were placed and the excreta samples were collected.

They were able to obtain many records in their camera traps and collected many samples of excreta. This diversity of data allowed them to conduct robust analyses. The data analyses carried out were adequate to obtain clear and meaningful results that enabled them to answer the research questions posed. The conclusions of this paper are mostly well supported by data.

The study has demonstrated the coexistence of carnivore species in the landscapes of the Qilian Mountains National Park, complementing the findings of previous studies. The information presented in this study is important for wildlife conservation and will contribute substantially to the current understanding of carnivore guilds and effective conservation management in fragile alpine ecosystems.

Weaknesses:

It is necessary to better explain the methodology because it is not clear what is the total sampling effort. In methodology, they only claim to have used 280 camera traps, and in the results, they mention that there are 319 sampling sites. However, the total sampling effort (e.g. total time of active camera traps) carried out in the study and at each site is not specified.

Reviewer #2 (Public Review):

Summary:

The study entitled "Different coexistence patterns between apex carnivores and mesocarnivores based on temporal, spatial, and dietary niche partitioning analysis in Qilian Mountain National Park, China" by Cong et al. addresses the compelling topic of carnivores' coexistence in a biodiversity hotspot in China. The study is interesting given it considers all three components affecting sympatric carnivores' distribution and co-occurrence, namely the temporal, the spatial, and the dietary partition within the carnivore guild. The authors have found that spatial co-occurrence is generally low, which represents the major strategy for coexistence, while there is temporal and dietary overlap. I also appreciated the huge sampling effort carried out for this study by the authors: they were able to deploy 280 camera trapping sites (which became 322 in the result section?) and collect a total of 480 scat samples. However, I have some concerns about the study on the non-consideration of the human dimension and potential anthropogenic disturbance that could affect the spatial and temporal distribution of carnivores, the choice of the statistical model to test co-occurrence, and the lack of clearly stated ecological hypotheses.

Strengths:

The strengths of the study are the investigation of all three major strategies that can mitigate carnivores' coexistence, therefore, the use of multiple monitoring techniques (both camera trapping and DNA metabarcoding) and the big dataset produced that consists of a very large sampled area with a noteworthy number of camera tap stations and many scat samples for each species.

Weaknesses:

I think that some parts of the manuscript should be written better and more clearly. A clear statement of the ecological hypotheses that could affect the partitioning among the carnivore guild is lacking. I think that the human component (thus anthropogenic disturbance) should have been considered more in the spatial analyses given it can influence the use of the environment by some carnivores. Additionally, a multi-species co-occurrence model would have been a more robust approach to test for spatial co-occurrence given it also considers imperfect detection.

Temporal and dietary results are solid and this latter in particular highlights a big predation pressure on some prey species such as the pika. This implies important conservation and management implications for this species, and therefore for the trophic chain, given that i) the pika population should be conserved and ii) a potential poisoning campaign against small mammals could be incredibly dangerous also for mesocarnivores feeding on them due to secondary poisoning.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This work explored intra and interspecific niche partitioning along spatial, temporal, and dietary niche partitioning between apex carnivores and mesocarnivores in the Qilian Mountain National Park of China, using camera trapping data and DNA metabarcoding sequencing data. They conclude that spatial niche partitioning plays a key role in facilitating the coexistence of apex carnivore species, spatial and temporal niche partitioning facilitate the coexistence of mesocarnivore species, and spatial and dietary niche partitioning facilitate the coexistence between apex and mesocarnivore species. The information presented in this study is important for wildlife conservation and will contribute substantially to the current understanding of carnivore guilds and effective conservation management in fragile alpine ecosystems.

Strengths:

Extensive fieldwork is evident in the study. Aiming to cover a large percentage of the Qilian Mountain National Park, the study area was subdivided into squares, as a geographical reference to distribute the sampling points where the camera traps were placed and the excreta samples were collected.

They were able to obtain many records in their camera traps and collected many samples of excreta. This diversity of data allowed them to conduct robust analyses. The data analyses carried out were adequate to obtain clear and meaningful results that enabled them to answer the research questions posed. The conclusions of this paper are mostly well supported by data.

The study has demonstrated the coexistence of carnivore species in the landscapes of the Qilian Mountains National Park, complementing the findings of previous studies. The information presented in this study is important for wildlife conservation and will contribute substantially to the current understanding of carnivore guilds and effective conservation management in fragile alpine ecosystems.

Weaknesses:

It is necessary to better explain the methodology because it is not clear what is the total sampling effort. In methodology, they only claim to have used 280 camera traps, and in the results, they mention that there are 319 sampling sites. However, the total sampling effort (e.g. total time of active camera traps) carried out in the study and at each site is not specified.

Thanks a lot for this detailed review! We apologize for not offering a distinct description of the overall sampling effort. In this study, we deployed 280 camera trappings, and these cameras were active for approximately 4 to 6 months. We visited each camera 2 to 3 times annually to download photos and check the batteries. In case some cameras failed to capture the targeted carnivore, we would relocate the positions of those cameras. Eventually, we collected 322 camera trapping sites, among which 3 cameras malfunctioned due to loss. As a result, we analyzed data from 319 camera sites and obtained 14,316 independent detections over 37,192 trap-days.

We have added this information as follows in lines 132 to lines 143: “Taking into account the fact that mammalian communities are sensitive to seasonality, we used camera traps to monitor animals with an extensive survey effort from December 2016 to February 2022, covering the activity of animal species in different seasons, which can reflect the overall distribution of carnivores. We placed a total of 280 infrared cameras at the study site, set them to be active for 4 to 6 months, and considered possible relocation to another position based on animal detection in an effort to improve estimates of the occupancy and detection rates for both common and rare species (Figure 1) (Kays et al., 2020). The camera trap was set to record the time and date on a 24 hr clock when triggered, and to record a 15s video and 1 photo with an interval of 2 minutes between any two consecutive triggers. The sum of camera trap effective days was defined by the total amount of trapping effort during the sampling period, which was calculated from the time the camera was placed in operation to the time the last video or photograph was taken. We visited each camera 2 to 3 times a year to download photos and check batteries.” and lines 228 to lines 232: “A total of 322 camera trap sites were surveyed after relocating infrared cameras that did not capture any target carnivore species. A total of 3 cameras were considered to have failed due to loss. We analyzed data from 319 camera sites and obtained 14,316 independent detections during a total effort of 37,192 effective camera trap days. We recorded wolf in 26 sites, snow leopard in 109 sites, Eurasian lynx in 36 sites, red fox in 92 sites, and Tibetan fox in 34 sites.”

Reviewer #2 (Public Review):

Summary:

The study entitled "Different coexistence patterns between apex carnivores and mesocarnivores based on temporal, spatial, and dietary niche partitioning analysis in Qilian Mountain National Park, China" by Cong et al. addresses the compelling topic of carnivores' coexistence in a biodiversity hotspot in China. The study is interesting given it considers all three components affecting sympatric carnivores' distribution and co-occurrence, namely the temporal, the spatial, and the dietary partition within the carnivore guild. The authors have found that spatial co-occurrence is generally low, which represents the major strategy for coexistence, while there is temporal and dietary overlap. I also appreciated the huge sampling effort carried out for this study by the authors: they were able to deploy 280 camera trapping sites (which became 322 in the result section?) and collect a total of 480 scat samples. However, I have some concerns about the study on the non-consideration of the human dimension and potential anthropogenic disturbance that could affect the spatial and temporal distribution of carnivores, the choice of the statistical model to test co-occurrence, and the lack of clearly stated ecological hypotheses.

Strengths:

The strengths of the study are the investigation of all three major strategies that can mitigate carnivores' coexistence, therefore, the use of multiple monitoring techniques (both camera trapping and DNA metabarcoding) and the big dataset produced that consists of a very large sampled area with a noteworthy number of camera trap stations and many scat samples for each species.

Weaknesses:

I think that some parts of the manuscript should be written better and more clearly. A clear statement of the ecological hypotheses that could affect the partitioning among the carnivore guild is lacking. I think that the human component (thus anthropogenic disturbance) should have been considered more in the spatial analyses given it can influence the use of the environment by some carnivores. Additionally, a multi-species co-occurrence model would have been a more robust approach to test for spatial co-occurrence given it also considers imperfect detection.

Thank you very much for your valuable comments and suggestions. We checked and edited the manuscript, and we thought the English level was improved.

(1) According to your suggestion, we added the competitive exclusion and niche differentiation hypothesis with space, time and diets axis to explain co-occurrence relationship among species in the introduction as follow: “The competitive exclusion principle dictates that species with similar ecological requirements are unable to successfully coexist (Hardin, 1960; Gause, 1934). Thus, carnivores within a guild occupy different ecological niches based on a combination of three niche dimensions, i.e. spatial, temporal, and trophic (Schoener, 1974). Spatially, carnivore species within the same geographic area exhibit distinct distributions that minimize overlap in resource use and competition. For example, carnivores can partition habitats based on habitat feature preferences and availability of prey (De Satgé et al., 2017; Garrote and Pérez De Ayala, 2019; Gołdyn et al., 2003; Strampelli et al., 2023). Temporally, differences in seasonal or daily activity patterns among sympatric carnivores can reduce competitive interactions and facilitate coexistence. For example, carnivores can exhibit temporal segregation in their foraging behaviors, such as diurnal versus nocturnal activity, to avoid direct competition (Finnegan et al., 2021; Nasanbat et al., 2021; Searle et al., 2021). Trophically, carnivore species can diversify their diets to exploit different prey species or sizes, thereby reducing competition for food resources. For example, carnivores can exhibit dietary specialization to optimize their foraging efficiency and minimize competitive pressures (Steinmetz et al., 2021).”

(2) In addition to distance from roads, we included human dimension as covariates influencing occupancy rates based on the number of independent photos or videos of herders and livestock detected by infrared cameras (named human disturbance and is represented by hdis). According to the results of occupancy models, we found red fox occupancy probability displayed a significant positive relationship with hdis. Moreover, the detection probability of snow leopard and Eurasian lynx decreased with increasing hdis.

We have incorporated these results into the Results as follow: “According to the findings derived from single-season, single-species occupancy models, the snow leopard demonstrated a notably higher probability of occupancy compared to other carnivore species, estimated at 0.437 (Table 1). Conversely, the Eurasian lynx exhibited a lower occupancy probability, estimated at 0.161. Further analysis revealed that the occupancy probabilities of the wolf and Eurasian lynx declined with increasing Normalized Difference Vegetation Index (NDVI) (Table 2, Figure 2). Additionally, wolf occupancy probability displayed a negative relationship with roughness index and a positive relationship with prey availability. Snow leopard occupancy probabilities exhibited a negative relationship with distance to roads and NDVI. In contrast, both red fox and Tibetan fox demonstrated a positive relationship with distance to roads. Moreover, red fox occupancy probability increased with higher human disturbance and greater prey availability. The detection probabilities of wolf, snow leopard, red fox, and Tibetan fox exhibited an increase with elevation (Table 2). Moreover, there was a positive relationship between the detection probability of Tibetan fox and prey availability. The detection probabilities of snow leopard and Eurasian lynx declined as human disturbance increased.”

(3) We appreciate the suggestion to use a multi-species co-occurrence model to test spatial co-occurrence. We attempted a multispecies occupancy modeling to analysis the five species in our study followed the method of Rota et al. (2016). Initially, we simplified the candidate models by adopting a single-season, single-species occupancy model. We selected occupancy covariates from the best model as the best covariates for each species and used them to establish multispecies occupancy models. Unfortunately, the final model results did not converge. We are investigating potential solutions to resolve this problem.

Rota CT, Ferreira MAR, Kays RW, Forrester TD, Kalies EL, McShea WJ, Parsons AW, Millspaugh JJ. 2016. A multispecies occupancy model for two or more interacting species. Methods Ecol Evol 7:1164–1173. doi:10.1111/2041-210X.12587

Temporal and dietary results are solid and this latter in particular highlights a big predation pressure on some prey species such as the pika. This implies important conservation and management implications for this species, and therefore for the trophic chain, given that i) the pika population should be conserved and ii) a potential poisoning campaign against small mammals could be incredibly dangerous also for mesocarnivores feeding on them due to secondary poisoning.

Thank you for your thoughtful comments. We appreciate your recognition of the temporal and dietary findings, particularly the highlighted predation pressure on prey species like the pika. These observations indeed underscore critical implications for conservation and management. The necessity to conserve the pika population is paramount for its role in maintaining the stability of the trophic chain within its ecosystem. As you rightly pointed out, any disruption to this delicate balance, including through predation or indirect threats like poisoning campaigns, could have far-reaching consequences. Regarding the potential risks associated with poisoning campaigns targeting small mammals, we acknowledge the significant concerns raised about secondary poisoning affecting mesocarnivores. This underscores the need for careful consideration in pest control strategies and the adoption of measures that minimize unintended ecological impacts. Our findings suggest several practical implications for conservation and management. Conservation efforts should focus on vulnerable prey populations such as the pika, while management strategies could include regulatory frameworks and community education to mitigate risks associated with pest control methods. We believe our study contributes valuable insights into the complexities of predator-prey dynamics and the broader implications for ecosystem health. By integrating these findings into conservation practices, we can work towards ensuring the sustainability of natural systems and the species that depend on them.

Reviewer #1 (Recommendations For The Authors):

To better explain the methodology and the sampling effort I recommend reviewing e.g. Kays et al. 2020. An empirical evaluation of camera trap study design: How many, how long, and when?. Methods in Ecology and Evolution, 11(6), 700-713. https://besjournals.onlinelibrary.wiley.com/doi/epdf/10.1111/2041-210X.13370.

Thank you for this valuable suggestion! According to this reference, we have added this information to explain the methodology and the sampling effort as follow: “Taking into account the fact that mammalian communities are sensitive to seasonality, we used camera traps to monitor animals with an extensive survey effort from December 2016 to February 2022, covering the activity of animal species in different seasons, which can reflect the overall distribution of carnivores. We placed a total of 280 infrared cameras at the study site, set them to be active for 4 to 6 months, and considered possible relocation to another position based on animal detection in an effort to improve estimates of the occupancy and detection rates for both common and rare species (Figure 1) (Kays et al., 2020). The camera trap was set to record the time and date on a 24 hr clock when triggered, and to record a 15s video and 1 photo with an interval of 2 minutes between any two consecutive triggers. The sum of camera trap effective days was defined by the total amount of trapping effort during the sampling period, which was calculated from the time the camera was placed in operation to the time the last video or photograph was taken. We visited each camera 2 to 3 times a year to download photos and check batteries.”

Reviewer #2 (Recommendations For The Authors):

I have some concerns about the manuscript.

I find that the manuscript should be written more clearly: some sentences are not straightforward to understand given the presence of structural errors that make the text hard to read; the paragraphs should be written in a more harmonic way (without logical leaps) with a smoother change of topic between paragraphs, especially in the introduction.

We appreciate your constructive comments, which have helped us improve the clarity and coherence of the manuscript. We have revised the introduction to provide a clearer outline of the paper's structure and objectives. Specifically, we have rephrased complex sentences and removed ambiguities to ensure that each idea is communicated more straightforwardly. We providing clearer links between ideas and avoiding abrupt shifts in topics to ensure that a smoother transition between paragraphs.

I feel like the strength of merging the two techniques (camera trapping and DNA metabarcoding) is not brought up enough, while the disadvantage of this approach is not even mentioned (e.g., the increasing costs).

Thanks a lot for this valuable comment! We have added this information to the Discussion (L356-L363) as follow: “Our study highlights the effectiveness of combining camera trapping with DNA metabarcoding for detecting and identifying both cryptic and rare species within a sympatric carnivore guild. This integrated approach allowed us to capture a more comprehensive view of species presence and interactions compared to traditional visual surveys. whereas, it is important to acknowledge the challenges associated with this technique, including the high costs of equipment and the need for specialized training and computational resources to manage and analyze the large volumes of sequence data. Despite these challenges, the benefits of this combined method in improving biodiversity assessments and understanding species coexistence outweigh the drawbacks.”

The structure of the manuscript does not follow the structure of the journal (Intro, Material and Method, Results, Discussion instead it reports the methods at the end of the main manuscript), and, most critically, I found that a clear explanation of the research hypothesis is missing: authors should clearly state they ecological hypotheses. What are your hypotheses on the co-occurrence relationship among species? What would specifically affect and change the sympatric relationships among carnivores?

Thank you for this valuable suggestion! We have revised the manuscript, that is integrated the methods section appropriately within the main body of the manuscript to ensure that it aligns with the standard sections (Introduction, Materials and Methods, Results, Discussion.

We state our main ecological hypotheses concerning the co-occurrence relationships among carnivore species is based on niche differentiation hypothesis. We hypothesize that differentiation along one or more niche axes is beneficial for the coexistence of carnivorous guild in the Qilian Mountains. We expected that spatial niche differentiation promotes the coexistence of large carnivores in the Qilian Mountain region, as they are more likely than small carnivores to spatially avoid interspecific competition (Davis et al., 2018). Mesocarnivores may coexist either spatially or temporally due to increased interspecific competition for similar prey (Di Bitetti et al., 2010; Donadio and Buskirk, 2006). Nutritional niche differentiation may be a significant factor for promoting coexistence between large and mesocarnivore species due to differences in body size (Gómez-Ortiz et al., 2015; Lanszki et al., 2019). We have added ecological hypotheses in lines 101 to 110.

Another concern is that all pictures with people have been removed from the dataset, but I think that this could be a bit biased as human presence (or also the presence of livestock) could affect the spatial or temporal presence of carnivores, changing their co-occurrence dynamics. On one side, humans can be perceived as a source of disturbance by carnivores and, therefore, can cause a shift in distribution towards locations with lower human presence (or lower anthropogenic disturbance) that could further concentrate the presence of carnivores increasing the competitive interaction. Conversely, mesocarnivores could take advantage of an increasing human presence - following the human shield hypotheses - finding a refugium from larger body carnivores. From this perspective, important information on the potential anthropogenic pressure is lacking in the description of the study area: how effective is the protection effort of the park? How intense is the potential human disturbance in and around the park? Is there poaching? Intensive livestock grazing? Resources extractions? These are all factors that could affect the interactions among carnivores. Do not forget the possibility and risk of being retaliatory killed by humans due to the presence of livestock in the area. I think that incorporating the human dimension is important because it could strongly affect how carnivores perceive and use the environment. Here only the distance to the closest road has been considered. However, for example, recent research (Gorczynski et al 2022, Global Change Biology) has indeed found that co-occurrece of ecologically similar species differed in relation to increasing human density. Therefore, I think that anthropogenic disturbance is an aspect to be reckoned with and more variables as proxy of human disturbance should be considered.

Thanks a lot for this valuable comment! We acknowledge that humans can act as both a disturbance factor, potentially driving carnivores away from highly populated areas, and as a source of indirect refuge for mesocarnivores, thereby affecting competitive interactions among carnivores. We understand that poaching and resource extraction are prohibited and livestock grazing is a significant human activity within the study area. Therefore, we added human dimension as covariates influencing occupancy rates based on the number of independent photos or videos of herders and livestock detected by infrared cameras (named human disturbance and is represented by hdis). According to the results of occupancy models, we found red fox occupancy probability displayed a significant positive relationship with hdis. Moreover, the detection probability of snow leopard and Eurasian lynx decreased with increasing hdis.

In the statistical analyses section, I don't find that the statistical procedure is well described: it is not clear which occupancy model has been used (probably a single-species single-season occupancy model for each target species?), which covariates have been tested for each species and following which hypotheses. Additionally, I think that when modelling the spatial distribution of subordinate species, it should be important to include information on the spatial distribution of apex species given this could affect their occurrence on the territory. This could have been done by using the Relative Abundance Index of the apex predators as a covariate when modelling the distribution of subordinate species. Additionally, why haven't the authors used prey as a covariate for occupancy? I think that prey distribution should affect the occupancy probability more than the detection rate. Also, the authors used the Sørensen similarity index to measure associations between species. However, this association metric has been criticized (see the recent paper of Mainali et al 2022, Science Advances). I am therefore wondering: given the authors are using the occupancy framework, why don't they use a multi-species co-occurrence model that allows them to directly estimate both single-species occupancy and the co-occurrence parameter as a function of covariates (examples are Rota et al. 2016, Methods Ecol. Evol. Or Tobler et al. 2019, Ecology)? For the temporal overlap, I think that adding Figure S2 (pairwise temporal overlap) in the main text would help deliver the results of the temporal analyses more straightforwardly.

Thanks a lot for this valuable comment!

(1) The current manuscript utilizes a single-species single-season occupancy model for each target species. Additionally, we have added prey and human disturbance as occupancy covariables. We have revised the statistical analyses section to explicitly state this model choice and clarify the covariates tested for each species from lines 153 to lines170. The details are as follows: “To investigate the spatial distribution of carnivores, as well as the influence of environmental factors on the site occupancy of species in the study area, we performed single-season, single-species occupancy models to estimate carnivores’ occupancy (ψ) and detection (Pr) probability (Li et al., 2022b; MacKenzie, 2018; Moreno-Sosa et al., 2022). To ensure capture independence, only photo or video records at intervals of 30 min were was included in the data analysis (Li et al., 2020). We created a matrix recording whether each carnivore species was detected (1) or not (0) across several 30-day intervals (that is 0-30, 31-60, 61-90, 91-120, 121-150, >150 days) for each camera location. Based on the previous studies of habitat use of carnivores (Greenspan and Giordano, 2021; Alexander et al., 2016; Gorczynski et al., 2022), we selected terrain, vegetation, biological factors and disturbance to construct the model. Terrain is a fundamental element of wildlife habitat and closely linked to other environmental factors (Chen et al., 2024). Terrain variables include elevation (ele) and roughness index (rix). Vegetation variables include normalized difference vegetation index (ndvi), and provide information on the level of habitat concealment. Biological variables include prey abundance (the number of independent photos of their preferred prey based on dietary analysis in this study, wolf and snow leopard: artiodactyla including livestock; Eurasian lynx and Pallas’s cat: lagomorpha; red fox and Tibetan fox: lagomorpha and rodentia) and reflect habitat preference and distribution patterns of carnivores. Disturbance variables include distance to roads (disrd) and human disturbances (hdis, the number of independent photos of herdsman and livestock) and can provide insight into the habitat selection and behavior patterns of carnivores.”

(2) Thank you for your valuable suggestions. We acknowledge the importance of considering apex species in models of subordinate species' spatial distributions.

Nonetheless, considering the consistency of covariates for each species and the lack of interspecies interactions in single-species occupancy models, we did not include the Relative Abundance Index of the apex predators as a covariate affecting the occupancy of mesopredators. As you recommended, multi-species occupancy models that account for interspecies interactions are a robust approach. However, we attempted to use the multi-species occupancy method of Rota et al. (Rota et al., 2016), the final model results did not converge. Specifically, we selected occupancy covariates from the best model by single-species model as the best covariates for each species and used them to establish multispecies occupancy models. We are investigating potential solutions to resolve this problem.

(3) We used the Sørensen similarity index to measure associations between species based on support from previous literature. As counted by Mainali et al., the Sørensen index has been used in more than 700 papers across journals such as Science, Nature, and PNAS. We believe this index holds broad applicability in describing relationships between species.

(4) We agree that presenting pairwise temporal overlap in the main text would enhance clarity. We revised the manuscript to include Figure S2 in the main text and ensure that the temporal analyses are more straightforwardly presented.

Regarding the sampling collection of the scats, I'm just curious to know why you decided to use silica desiccant instead of keeping the samples frozen. I'm not familiar with this method and I guess it works fine because the environment is generally freezing cold. Yet, I would like to know more. How fresh do scat samples need to be in order to be suitable for DNA metabarcoding analyses? Additionally, what do you mean by "scats were collected within camera trapping area", could you be more specific? Have you specified a buffer around camera stations?

Thanks a lot for this specific inquiry! We refer to the scat collection method mentioned in the study of Janecka et al (2008; 2011). Silica is used to dry the scats to minimize DNA degradation. Due to the limitation of field environmental conditions, there is no suitable equipment to freeze samples during sampling, the collected scat samples should be kept dry and cool in shade, and transferred to the laboratory as soon as possible after sampling. We selected relatively fresh samples based on the color of the scat as well as broken off bits and pieces from the outside part of the scat including pieces not directly in the sun. Collect scat material about the size of a pinkie nail in the tube. If over fill the tube it will likely not dry and lead to DNA degradation.

The study area was subdivided into sample squares of 25 km2 (5×5 km) as a geographical reference for placing camera survey sites and collecting scat samples. Camera traps were set in areas believed to be important to and heavily used by wildlife, such as the bottoms of cliffs, sides of boulders, valleys and ridges along movement corridors. Also, we focused on sites with known or suspected carnivore activity to maximize probability of detection for scat samples. Therefore, transects were set around the infrared camera to collect scat samples. Length of each transect was determined by terrain, amount of scat, and available time. Each transect should have collected about 18 samples or covered 5 km of terrain to avoid uneven representation among transects and ensure that the team has sufficient time to return to base camp (Janečka et al., 2011).

Janecka J, Jackson R, Yuquang Z, Li D, Munkhtsog B, Buckley-Beason V, Murphy W. 2008. Population monitoring of snow leopards using noninvasive collection of scat samples: A pilot study. Animal Conservation 11:401–411. doi:10.1111/j.1469-1795.2008.00195.x

Janečka JE, Munkhtsog B, Jackson RM, Naranbaatar G, Mallon DP, Murphy WJ. 2011. Comparison of noninvasive genetic and camera-trapping techniques for surveying snow leopards. J Mammal 92:771–783. doi:10.1644/10-MAMM-A-036.1

Kays R, Arbogast BS, Baker‐Whatton M, Beirne C, Boone HM, Bowler M, Burneo SF, Cove MV, Ding P, Espinosa S, Gonçalves ALS, Hansen CP, Jansen PA, Kolowski JM, Knowles TW, Lima MGM, Millspaugh J, McShea WJ, Pacifici K, Parsons AW, Pease BS, Rovero F, Santos F, Schuttler SG, Sheil D, Si X, Snider M, Spironello WR. 2020. An empirical evaluation of camera trap study design: How many, how long and when? Methods Ecol Evol 11:700–713. doi:10.1111/2041-210X.13370

Regarding the discussion, the authors have information for 1) spatial distribution, 2) temporal overlap, 3) dietary requirement, they should use this information to support the discussion. Instead, sometimes it feels that authors go by exclusion or make a suggestion. For example: the authors have found dietary and temporal overlap between two apex predators (i.e., wolf and snow leopard), and they said that this suggests that spatial partitioning is responsible for their successful coexistence in this area (lines 195-196). But why "suggesting", what the co-occurrence metric says? Another example: "Apex carnivores and mesocarnivores showed substantial overlap in time overall, indicating that spatial and dietary partitioning may play a large role in facilitating their coexistence" (lines 241 - 242). However, this should not be a suggestion: your Sørensen similarity index is low proving spatial divergence. So, when data supports the hypotheses, the authors should be firmer in their discussion. Generally, when reading the discussion, it felt that a figure summarizing the partitioning would be much needed to digest which type of partitioning strategy the species are using.

Thank you for your thoughtful comments and suggestions.

(1) We appreciate your insights on the discussion section, particularly concerning the interpretation of our findings on spatial distribution, temporal and dietary overlap. We acknowledge the need for clearer interpretation of our findings. We have revised the discussion section to provide more direct support. For example, in line 294-295, we modify it as “We found dietary and temporal overlap among apex carnivores, showing that spatial partitioning is responsible for their successful coexistence in this area.” In line 341-342, we modify it as “Apex carnivores and mesocarnivores exhibited considerable overlap in time overall, showing that spatial and dietary partitioning may play a large role in facilitating their coexistence.”

(2) We appreciate your suggestion regarding the inclusion of a figure summarizing partitioning strategies among species discussed. In our study, we organized the overlap index of space, time, and diet among carnivores in Table 3, which directly reflects the overlap of carnivore species in these three dimensions by summarizing them in a single table. Additionally, Figure 3 illustrates the activity patterns and overlap among species, while Figure 4 displays the primary prey of carnivores and the frequency of food utilization.

About lines 228 - 229, just as a side note, the Pallas's cat, as the red fox, selects the environment according to a greater distribution of prey species, while also selecting primarily meadows and natural environment (Greco et al. 2022, Journal of wildlife management) additionally it is not strictly diurnal (Anile et al. 2020, Wildlife Research; Greco et al. 2022, Journal of wildlife management). Regarding the Pallas's cat and its exclusion from the temporal and spatial analyses, can you specify how many independent detection events you had?

Thanks a lot for this valuable comment!

(1) We appreciate the references to recent studies highlighting its habitat preferences and activity patterns. We have revised the manuscript to acknowledge these points and provide context regarding its habitat selection strategies. Specifically, we modify it as follow: “Pallas’s cat hunts during crepuscular and diurnal periods, inhabits meadow with greater prey abundance (Anile et al., 2021; Greco et al., 2022; Ross et al., 2019).”

(2) The low detection rate of Pallas's cat (0.072) identified by single-species occupancy model raised concerns regarding the reliability of the results. The estimated high standard errors for each environmental variable and the wide confidence intervals around the detection rate further indicated potential bias or randomness. Consequently, we made the decision to exclude the Pallas's cat data from further analysis. Upon closer examination of the Pallas's cat data, it became evident that out of 319 camera sites surveyed, only 27 sites detected the presence of Pallas's cat. Notably, only 3 out of 193 sites in Gansu Province recorded detections, while Qinghai Province had 24 detections out of 126 sites. This skewed distribution of data likely contributed to the unsatisfactory outcomes observed in our models.

About the diet and results of scat analyses, have you found any sign of intra-guild predation (i.e., apex predators that kill and sometimes consume subordinate carnivores to reduce competition), this could actually represent proof of competition and spatial overlap.

Thanks a lot for your thoughtful comments!

We observed intraguild predation in the diet of wolves and snow leopards. Specifically, we found the presence of Pallas’s cat, red fox, and Tibetan fox in the diet of wolfs, and Pallas’s cat, Eurasian Badger and Tibetan fox in the diet of snow leopard. However, these intraguild predation events accounted for only 1.89% of the diet composition of apex carnivores. We suggest that the rarity of these observations may be influenced by various factors and does not necessarily provide sufficient evidence of competition and spatial overlap. Therefore, further data collection and in-depth research are needed to better understand this phenomenon.

Some minor comments: Figure 2 is really nice, while some abbreviations are missing in the caption of Table 2.

Thank you for your feedback and positive comments on Figure 2. Unfortunately, we have removed Figure 2 from the manuscript. Due to the inclusion of prey abundance and human disturbance as occupancy covariates, these variables were derived solely from infrared camera trap data and did not encompass a comprehensive dataset across the entire national park. Therefore, we were unable to accurately spatially project for carnivore species occupancy probability in nature park.

We apologize for the oversight that the abbreviations missing in the caption of Table 2. We have added the missing abbreviations to the caption of Table 2 as follow: “Abbreviations: Disrd-distance to roads, Ele-elevation, NDVI-normalized difference vegetation index, Rix- roughness index, hdis-human disturbance.”

eLife assessment

This important study shows that a splice variant of the kainate receptor Glu1-1a that inserts 15 amino acids in the extracellular N-terminal region substantially changes the channel's desensitization properties, the sensitivity to glutamate and kainate, and the effects of modulatory Neto proteins. In the revised paper the authors have clarified several points raised by reviewers but the structural portion of the study has not been improved and consequently, more data are needed to determine the molecular mechanism by which the insert changes the functional profile of the channel. Even so, these solid findings advance our understanding of splice variants among glutamate receptors and will be of interest to neuro- and cell-biologists and biophysicists in the field.

Reviewer #1 (Public Review):

Kainate receptors play various important roles in synaptic transmission. The receptors can be divided into low affinity kainate receptors (GluK1-3) and high affinity kainate receptos (GluK4-5). The receptors can assemble as homomers (GluK1-3) or low-high affinity heteromers (GluK4-5). The functional diversity is further increased by RNA splicing. Previous studies have investigated C-terminal splice variants of GluK1, but GluK1 N-terminal (exon 9) insertions have not been previously characterized. In this study Dhingra et al investigate the functional implications of a GluK1 splice variant that inserts a 15 amino acid segment into the extracellular N-terminal region of the protein using whole-cell and excised outside-out electrophysiology.<br /> The authors convincingly show that the insertion profoundly impacts the function of GluK1-1a - the channels that have the insertion are slower to desensitize. The data also shows that the insertion changes the modulatory effects of Neto proteins, resulting in altered rates of desensitization and recovery from desensitization. To determine the mechanism by which the insertion exerts these functional effects, the authors perform pull-down assays of Neto proteins, and extensive mutagenesis on the insert.<br /> The electrophysiological part of the study is very rigorous and meticulous.

The biggest weakness of the manuscript is the structural work. Due to issues with preferred orientation (a common problem in cryo-EM), the 3D reconstructions are at a low resolution (in the 5-8 Å range) and cannot offer much mechanistic insight into the effects of the insertion. Based on the available data, the authors posit that the insertion does not change the arrangement of the subunits in the desensitized state. However, there is no comparison with a structure that does not contain the insertion, so while the statement may well be true, no data is shown to support it.

Overall, the cryo-EM contributes little and distracts from the good parts of the manuscript.

Another part that does not contribute much is the RNAseq data that has been pulled from a database and analyzed for the paper. It is being used to show that the exon 9 insertion variant is predominantly expressed in the cerebellar cortex at early stages of brain development. The methods do not describe in detail how the data has been analyzed (e.g., is the data scaled per sample/gene or globally?) so it is hard to know what we can compare in the heat plots. In Figure 1- supplement 1 there aren't striking differences in expression (at least not obviously visible in the current illustration).

Despite these weaknesses, the study is a valuable contribution to the field because it characterizes a GluK1 variant that has not been studied before and highlights the functional diversity that exists within the kainate receptor family.

Revised manuscript:

The authors have clarified some of the issues raised by the reviewers, but no new data has been added to strengthen the manuscript. The structural part of the manuscript remains its weakest point, and the extent of mechanistic insight remains low.

Reviewer #2 (Public Review):

Among ionotropic glutamate receptors, kainate receptors (KAR) are still the object of intense investigation to understand their role in normal and pathological excitatory synaptic transmission. Like other receptors, KAR appear under different splicing variants and their respective physiological function is still debated. In this manuscript, Dhingra et al explored the impact of the presence and of the absence of Exon9 of the GluK1 receptors on the pharmacological, biophysi cal and structural properties of the receptors. They further investigated how it is impacted by the association of KAR with their cognate auxiliary subunit Neto 1 and 2. This study represents a large body of work and data. The authors addressed the issue in a very systematic and rigorous manner.

First, by exploring RNAseq database, authors showed that GluK1 transcripts containing the exon 9 are present in many brain structures and especially in the cerebellum suggesting that a large part of GluK1 contains effectively this exon9.<br /> Using HEK cells as an expression system, they characterized many gating and biophysical properties of GluK1 receptors containing or not the exon9. Evaluated parameters were desensitization, relative potency of glutamate versus kainate, and polyamine block.

It is known that the association of GluK1 with auxiliary proteins Neto1/2 modulates the properties of the receptors. Authors investigated systematically whether Neto1 and 2 similarly alter GluK1 properties in function of the presence of exon9. This study provides many quantitative data that could be reused for modeling the role of kainate receptors. Given the change shown by the authors, the presence of exon in GluK1 is noticeable and likely should have an impact of synaptic transmission.<br /> Interestingly, authors used a mutational approach to identify critical residues encoded by exon9 that are responsible for the functional differences between the two splice variants. In many cases, the replacement of a single amino acid leads to the absence of current confirming the crucial role of the segment of the receptor. However, it made the comparison and the identification of critical residues more challenging.

Authors attempted to establish the structure GluK1 receptors comprising the exon9 using different preparation methods. They succeeded in obtaining structures with equivalent or lower resolution compared with previous reports on GluK1 and GluK2 receptors. However, the organization of the peptide coded by exon is poorly defined and limited possible analyses. Despite this, they could observe that the presence of the exon9 does not alter significantly the structure of GluK1.

Reviewer #3 (Public Review):

GluK1 forms glutamate-gated ion channels with an important function in synaptic transmission and neuronal excitability. Alternative RNA splicing has been described for these channels, allowing the diversification of GluK1 channels. The GluK1 splice variant GluK1-1a contains 15 residues in the amino-terminal domain, resulting from the Exon 9 splice insert. GluK1-1a displays significant expression in different regions of the brain, likely co-expressing with other Gluk channels. The impact of the 15 residues on GluK1 channel properties and the overall structure has not been studied yet. The paper by Dhingra et al. aims to evaluate the impact of the Exon 9 splice insert on GluK1.1 channel function and structure. This work uses electrophysiological approaches, including whole-cell and patch clamp recordings, to determine the effect of the splice insert on GluK1.1 gating properties, including desensitization, agonist efficacy, recovery from desensitization, and rectification. By using mutagenesis and biochemical approaches, the authors studied the role of positively charged residues in the splice insert on channel properties and the interaction with modulatory Neto proteins. This work also shows the effect of the splice insert on the regulation of GluK1 channels by Neto proteins. Finally, by using Cryo-EM and single-particle analysis, the authors reconstructed a model for a homomeric GluK1-1a channel. Overall, this work provides two major milestones: 1) the first functional characterization of the GluK1-1a variant and 2) the first structure of this channel.

The functional data supporting the role of the insert on channel properties is convincing, although the current data does not provide significant insights about the mechanism. The overall structure in a putative desensitized state shows no differences with channels lacking the splice insert. However, some domains, including most of the 15 residues unique for the GluK1-1a variant were not resolved, suggesting high flexibility or conformational heterogeneity in those regions. Also, the low resolution of the obtained structures precludes conclusions on the structural basis for the role of the insert in channel function/regulation. Nonetheless, this paper represents an important advance in the study of glutamate receptors and invites the field to elucidate the structural basis for gating properties in GluK1-1a channels as well as other glutamate receptors. A more in-depth study about the role of splicing variants on ligand binding affinity, regulation by modulatory subunits such as Neto proteins, and the potential impact of this specific variant on heteromeric channels would also be relevant.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Recommendations For The Authors):

In its current form, I would exclude the cryo-EM data from the manuscript. It does not add much and it is distracting from the excellent work that you did on the functional characterization of the variant. Alternatively, you could try to improve the resolution and see if you can get some more meaningful analysis out of the structures? I noticed that you only collected very small datasets. If you decide to pursue a higher resolution reconstruction, collecting more movies will give you a better chance to obtain a higher resolution.

We express our gratitude to the reviewer for their invaluable feedback. While acknowledging that our structure currently maintains a low resolution, it still provides valuable insights into the splice's proximity to the N412 glycan density. This proximity and low-resolution map hindered the complete modeling of all the splice residues. Notably, this structure represents the first depiction of this particular splice variant. Consequently, it lays a foundation for subsequent studies in the field, and hence, we would want to keep it in the manuscript. As per reviewers’ suggestions, we have now included comparisons of our structure with the GluK1-2a receptor structure reported recently (Mayerson et al. 2022). We do plan to carry out higher-resolution structures in the future.

I would probably also exclude the RNAseq analysis. I think that Figure 1 is fine, but the supplement 1 is not very successful in convincing me that the exon 9 is expressed mainly in early stages of brain development. In addition, the plot in Figure 1 indicates strong expression in the cerebellar cortex in 20s and 30s. If you decide to keep the data, I strongly encourage you to include more details on the analysis in the methods section.

Thanks for this insightful comment. We have now modified this section extensively for better clarity. Indeed, the expression of this variant seems to be dynamic in different brain regions. This has now been specified in the revised manuscript. Figure 1 shows the expression of GRIK1 exon 9 gene in different regions of the human brain and donor age. The supplementary figure 1 is a zoom-in on one such region, the Cerebral cortex, where we observe the maximum expression of GRIK1. In this region, we also observed higher expression of exon 9 in the early stages of development. The scales of Figure 1 (0-4 RPKM) and supplemental Figure 1(06RPKM) are different due to more expression of other exons in supplemental Figure 1 (example, we observe 4RPKM expression in the shade of red, for figure 1, whereas similar values of 4RPKM are orange-yellow in the supplemental figure1). Using Supplemental Figure 1, we wanted to show the expression of exon 9 with respect to other exons during developmental stages that prove that GluK1-1 is highly expressed in the initial stages of life. more details on the analysis in the methods section has been added now.

Additionally, there are a few minor issues in the data presentation:

(1) in Fig. 2C there seems to be a mismatch between the green dose response plot and the GluK12a trace shown. The plot reports an EC50 of 187.7 uM, whereas in the sample trace 0.25 mM agonist activates only to ~20%.

We have verified the data and statistics, confirming their consistency with the values reported in the manuscript. For Figure 2C, we present representative traces from a single cell. However, the EC50 value was calculated using Hill's equation based on averaged data from 5 cells.

(2) The axis label is misprinted in Figure 3C

Thanks. Corrected.

(3) In Fig 5 supplement 1, panel B - the 3 last labels above the western blot lanes are off so it is difficult to see which sample corresponds to which lane.

Thanks. We have corrected the figure.

Reviewer #2 (Recommendations For The Authors):

Overall I congratulate the authors of this study nicely done. It represents a large body of work.

We thank the reviewer for his/her time and positive comments.

I have several minor corrections that authors could consider for the revision of the manuscript P7. The desensitization rate of GluK1-2a was "delayed"... replace by "increased".

Corrected.

P9. Last line 0.37; P.. Add the P value.

P value has been added as suggested.

P11 authors indicate that K368/375//379/382H376-E mutant exhibit significant difference in desensitization properties in presence of NEto1, but on the 1st line of p11, they provide a P value above 0.05

We thank the reviewer for pointing out this discrepancy and have fixed the same. We have discussed two mutants that show slower desensitization when compared to GluK1-1a co-expressed with Neto1. The K to E mutant has significance, while the des value for the K368/375//379/382H376-E mutant shows the same pattern, though not significantly. We have now modified the text to explain this more clearly.

P19 the calculation of mean weighted tau TDes is not clear and should be better explained.

Thanks. We have added more details in the Methods sections. We analyzed the current decays in response to 1–2 ms or 1 s applications by employing an exponential function or the sum of two exponential functions. This analysis allowed us to derive a weighted mean τdes using the formula [(τ1 × amplitude1) + (τ2 × amplitude2)]/[amplitude1 + amplitude2]. The tau values represent the time constants obtained from the exponential fits, while the amplitudes correspond to the estimated contributions of each component to the total peak current amplitude.

[(A1 * t1) + (A2 * t2)] / (A1 + A2)

It represents the calculation of a weighted mean, where A1 and A2 are the amplitudes, and t1 and t2 are the corresponding time constants. The formula calculates the overall mean time constant by taking into account the contribution of each component to the total amplitude.

P19 the rate of recovery was obtained by fitting the one-phase association "with" exponential function. With is missing.

We have corrected this error.  Thanks.

P21 which method has been used for site directed mutagenesis

Overlapping PCR was carried out for mutagenesis using the primers listed in Figure 4-table supplement 1. A ligation-free cloning approach (Zhang et al., 2017) was used. It has now been elaborated in the methodology section under Site directed mutagenesis.

P21 and 22. Provide complete reference of reagent including species of antibodies.

Thanks. We have added all the details in the methods section now. 

Anti-His: Rabbit mAb #12698 (Cell Signaling Technology)

Anti-Neto1: Rabbit #SAB3500679 (Sigma Aldrich)

Anti-GFP: Mouse mAb G1546 (Sigma Aldrich)

Anti-actin: Mouse mAb A3853 (Sigma Aldrich)

P22 How much anti His antibody was used with 40microliter of protein A?

We have used 2µg/ 40uL of Protein A slurry. This has now been added to the methodology.

P23 Authors seem to have used a virus to express protein but the protocol is not given. For example what is P2 virus?

We have now modified the manuscript to include details of baculovirus generation as per the protocol described in Goehring et al. 2014. We followed the same protocol wherein the 2nd generation of virus (P2) generated in insect (SF9) cells was used for infecting suspensionadapted HEK293-T cells for large-scale GluK1-1aEM protein expression.

Reviewer #3 (Recommendations For The Authors):

Major concerns:

(1) The effect of the splice insert on Gluk1 regulation by Neto proteins is not fully clear. For example, experiments in Fig. 3G indicate that the desensitization time for Gluk1-1a + Neto2 is ~32ms. This value is half compared with data obtained from whole-cell experiments shown in Fig. 3A (~70ms). What is the reason for this discrepancy? If variability is observed between experiments, I wonder how valid are the comparisons made in panel A between GluK11a+Neto2 vs GluK1-2a+Neto2 groups. In the case of recovery analysis, authors found significant differences comparing both groups in the presence of Neto (Fig. 3B) but recovery times are not identic for Gluk1-1a vs Gluk1-2a (without Neto). Thus, I wonder if the fold change related to the control group (without Neto) is different. 

We appreciate your detailed feedback, which has allowed us to clarify and reinforce the validity of our experimental findings. Different recording configurations (e.g., outside-out patch (Fig. 3G) versus whole-cell recordings (Fig. 3A) have been used. Whole-cell recordings average responses over a larger membrane area and also have slower solution exchange times compared to outside-out patch recordings. This may have contributed to the variability in desensitization times. However, similar trends in our whole cell vs. outside-out patch recordings were observed. Further, all the data except those presented in Figs 3G and 3H are from whole-cell recordings. We have performed multiple independent experiments and utilized rigorous statistical analyses to validate our comparisons. We report mean values with standard deviations or confidence intervals to provide a more accurate representation of the data.

Neto1 significantly speeds up the recovery from desensitization for both variants, with a more pronounced effect on GluK1-1a (GluK1-1a +Neto1: 0.68 s) compared to GluK1-2a (GluK1-2a +Neto1: 1.15 s). The recovery times are not identical for the two variants, likely due to the presence of splice insert in GluK1-1a. Neto2, on the other hand, slows recovery for both variants without significant differential effects. However, the recovery rate from the desensitized state is faster for GluK1-1 compared to GluK1-2a alone, although insignificant (without Neto). 

In the case of the glutamate concentration-response curve (Fig. 3C), EC50 values for Neto1 and Neto2 are relatively the same, but this approach on its own does not provide insights about the role of the splice insert. Previous experiments with the Gluk1 reveal differences between EC50 in the presence of Neto1 or 2 (Fisher, 2015), suggesting that the insert could regulate glutamate binding affinity, but still, this point is not directly demonstrated in this work.

Thanks for this insightful comment. Indeed, we cannot conclude that splice residues directly affect glutamate sensitivity and have modified the text accordingly. The Fisher paper demonstrated that both Neto1 and Neto2 can influence glutamate sensitivity in GluK1-2a, with EC50 values of 124.6 ± 16.2 µM. Specifically, in the presence of Neto1 and Neto2, the EC50 values are 4.4 ± 0.4 µM and 13.7 ± 4.2 µM, respectively, indicating a noticeable effect though not substantially different for GluK1-2a coexpressed with either Neto1 and Neto2. Our observation for the GluK1-1a has been similar, with both Neto1 and Neto2 showing a leftward shift.

(2) Similar to the previous point, a proper interpretation of mutant data is missing in the manuscript. From current data, it is difficult to visualize the role of the insert on Netodependent regulation, mainly, because of the fact that some mutations alone affect Gluk1-1 channel properties. The authors conclude their data by stating that "while the modulation of the receptor by Neto 1 is affected by mutations in splice insert, the modulation by Neto 2 remains largely unaffected" (Page 13). However, this statement is confusing since the co-expression of Gluk1-1a with Neto2 (Fig. 5) prevents the effect caused by mutation K368 alone (Fig. 4), indicating that modulations by Neto 2 are indeed potentially affected by the mutations. Please, clarify. Also, the effect of the K368/375/379/382H376-E mutant on Neto modulation (pink bar in Fig. 5) is impossible to interpret properly since the effect of the mutation alone is not shown in the manuscript.

Thanks for seeking this important clarification. It is indeed true that splice residue mutations themselves affect the receptor functional properties in comparison to the wild-type receptors. For the sake of clarity, we have presented the effect of splice mutants on receptor properties separately from the effect of mutations on modulation by Neto proteins. Figure 4 demonstrates a comparison between wild-type and mutant receptors without the Neto proteins, showcasing different kinetic properties, while Figure 5 provides detailed information on the role of the insert in Neto-dependent regulation. 

It’s true we could not record the effect of the K368/375/379/382H376-E mutant alone or when coexpressed with Neto 2 due to low peak amplitudes (mentioned in Table 1) that prevented reliable comparisons. However, robust currents were observed when the same mutant was coexpressed with Neto1, and hence comparisons were shown for this mutant with GluK1-1a wild-type + Neto1. 

We have now modified the statement "while the modulation of the receptor by Neto 1 is affected by mutations in splice insert, the modulation by Neto 2 remains largely unaffected" and the last paragraph as follows:

“Neto1 appears to have more pronounced effects on the mutant receptors compared to Neto2. Specifically, Neto1 significantly slowed desensitization for the K368-E mutant, accelerated recovery from desensitization for K368-E and K368/375/379/382H376-E mutants, increased agonist efficacy for K368-E and K375/379/382H376-E mutants, and altered rectification properties for K368E and K368/375/379/382H376-E mutants. In contrast, Neto2 had fewer significant effects on the mutant receptors, with the main impact being an increase in agonist efficacy for the K368-E mutant. Notably, Neto2 did not significantly affect desensitization, recovery from desensitization, or rectification properties of the mutant receptors when compared with wildtype GluK1-1a coexpressed with Neto2. These findings suggest that the splice residues in GluK1-1a differentially influence receptor modulation by Neto1 and Neto2, with Neto1 showing more extensive modulation of the mutant receptors' functional properties.”

(3) An open question after reading this interesting work is if the proposed change in Neto regulation because of the splice insert is due to changes in Gluk1-Neto interactions or because the rearrangement after interaction with Neto proteins is different. Pull-down experiments (Fig 5 Sup.1) suggest that the splice insert and all the mutants tested do not prevent interaction with Neto proteins. I wonder if the authors could complement their data with a quantitative approach/analysis to demonstrate if the splice insert and the mutants affect Neto1/2 interactions (as expected for the rationale when creating the mutants).

Thank you for this insightful suggestion. You raise an important point about distinguishing between changes in GluK1-Neto interactions and potential differences in receptor rearrangement after Neto binding. While our pull-down experiments suggest that the splice insert and mutants don't prevent Neto interactions (probably due to a larger interaction interface all along the receptor), a quantitative approach would indeed provide more nuanced information. In future studies, we do plan to perform a quantitative approach like Surface plasmon resonance to assess the changes in interactions upon mutations in the splice and/or Neto proteins in different states of the receptor. In addition, obtaining cryo-EM structures of GluK1 splice variants in complex with Neto1 and Neto2 would provide crucial insights into their interaction interfaces and any conformational changes induced by binding. 

(4) Related to the Gluk1-1a structure, the authors state that the overall structure is similar to the one without the insert (page 14); however, this is not properly shown in the manuscript. Even if the overall architecture of the channel is the same, authors should make a proper/adequate comparison between both structures/domains to support their claims. Also, one should expect that the insertion of 15 amino acids would affect in some way the closing neighboring domains. The differential effect of the splice insert on glutamate and kainate EC50 values (Fig. 2 and Fig. 2 sup.1), suggests that the insert could introduce a sort of rearrangement in the binding domain. Thus, I wonder if a more elaborated analysis of the current structural data could reveal some structural insights that would explain the specific functional differences due to the splice insert. If the low resolution and the missing residues avoid making some comparisons and establish differences between sidechain orientations, still, a proper comparison between the domain backbones would be helpful to validate the author's statement at least. Also, I wonder if the changes could be resolved better in a closed state or APO structure, instead of the desensitized structure. Finally, are the structures obtained in DDM and nanodiscs similar?

As per the reviewer’s suggestion, we have now added a new figure in the supplementary information, “Figure 6-figure supplement 9,” where we show a superimposition of GluK11aEM (detergent-solubilized or reconstituted in nanodiscs) and GluK1-2a (PDB:7LVT; silver) showing overall conservation of the structures in the desensitized state.

As evident from the figure and rmsd values mentioned above, we do not observe significant movements at both ATD and LBD layers of GluK1-1a with respect to GluK1-2a. Also as can be observed the DDM solubilized and nanodisc reconstituted GluK1-1a (Panel A) are very similar with a rmsd of ~2.19Å across all the 2664 Calpha atom pairs. Due to low resolution of our structures, we have refrained from carrying out detailed structural comparisions.

Our efforts to capture the closed state or apo state structures have failed due to either severe orientation bias (only top views) or increased heterogeneity. 

(5) Methods section lacks relevant information for proper data interpretation as well as for replicating some experiments in the future. For example:

A) The experimental design to determine the rectification index with a Ramp protocol is not clear: 1) Why the authors applied a ramp protocol if receptors desensitize along the time? Please clarify the protocol.

Ramp protocols were used only for the wild-type receptors to compare their voltage-dependent behavior, as this was the first study to compare the two splice variants. All kainate receptors (GluK1-GluK5) desensitize over time. However, their rectification properties have been studied previously (both the absence and presence of Neto proteins) using Ramp protocols as they are faster than step protocols.  

B) Are polyamines included in the solutions to perform the rectification assays?

No, polyamines were not added to the intracellular solution, and the effect of the endogenous polyamine block was measured. This has now been specified in the results as well as the methods section.

C) It is not clear if the experiments to calculate IK/IG ratios were performed in the same preparation (This is, the same cell was stimulated with glutamate and then kainate or vice versa).

Indeed, the current responses for glutamate vs kainate are performed in the same cell (the same cell was stimulated by glutamate then kainate) so that the responses can be compared. It’s now been specified in the methods section.

D) The experimental design for calculating recovery is not clear.

We employed a double pulse protocol to measure receptor recovery. The protocol involved applying two consecutive pulses of agonist stimulation to the receptor. Initially, we applied a brief agonist pulse to activate the receptor, followed by a specific recovery period. After the recovery period, we administered a second agonist pulse to assess the receptor's recovery response. The receptor's recovery was determined by comparing the response amplitude of the second pulse to that of the first pulse, providing valuable insights into the receptor's recovery kinetics. Recovery rates were calculated with single exponential association fits in Prism. We have now modified the text for better clarity.

E) Please indicate the species used for both functional and Cryo-EM (rat Gluk1 isoform?).

Thanks for pointing this out. We have now specified in relevant methodology sections that Rattus norvegicus GluK1 and Neto proteins were used in this study.

F) Please describe the nanodisc reconstitution protocol and how the nanodisc protein was purified, if appropriate.

The MSP1E3D1 was purified by following the protocol given by the Sligar group in 2014 (doi: 10.1016/S0076-6879(09)64011-8). The nanodisc reconstitution protocol has now been elaborated in the revised manuscript.

G) Site-directed mutagenesis methodology is incomplete. Please check.

We have now elaborated this section to include more details.

Minor concerns:

(1) Authors state that splice residues are ~30A away from the TM domain. Currently, there is no friendly representation showing the localization of the splice in the structure, besides Fig.6E. The manuscript could benefit itself if authors include a better 3D representation or a scheme to highlight the position of the splice relative to critical domains.

Thanks for pointing this out. The distance between TRP 381 CA (ATD) and LEU 636 CA (TM3) is 92.10 Å. We have changed the value in the text to ~92 Å.

Author response image 1.

(2) Authors mention that mutations in the insert to alanine show normal traffic to the plasma membrane but low current amplitude. Then, I wonder if single-channel conductance, mean open time or open probability is affected by the splice insert. Showing the effects of the insert on single-channel properties would strengthen the manuscript's quality.

It is a good suggestion. However, as can be observed from our whole cell or outside out patch data, we obtained low peak amplitudes (<50 pA) for many of our receptor-only constructs and also suffered from high SEM for some recordings due to heterogeneity between cells of the same population. The suggestion to study the single channel properties of these receptors is considered for future experiments

(3) It is unclear how the insert or the mutations specifically affect glutamate- or kainate-induced responses because authors analyze IK/IG ratios only. Maybe authors could consider including an analysis of the role of the insert on specific glutamate- or kainate-induced response to gain insights about ligand selectivity.

All the values have been included in the excel for raw data. We have included the desensitization kinetics of mutant receptors in the presence of glutamate and compared it to the wild type GluK1-1a. Kainate induced responses were very heterogenous (high SEM for % desensitization) and hence have not been included in the main data.

(4) Please be consistent with nomenclature along the manuscript to avoid confusion. For example, Are Gluk-1-1 and Gluk-1-1a referring to the same variant?

GluK1-1 has been used in the abstract and the introduction where we introduce the N-terminal splice variant which either has the 15 residues (termed as GluK1-1) or lacks it (GluK1-2). The C- terminal splice variants for GluK1 are named as “a-d”, with “a” being the smallest Cterminal domain variant. Later in the manuscript, we have used only GluK1-1a terminology to represent the ATD splice variant with shortest C-terminal domain.

The introduction and spatiotemporal results talk about the GluK1-1 receptors wherein the 

(5) Legend figure 2: Repeated phrase should be removed. Please check.

(6) Page 8: "This is similar to the effect observed in GluK1-2 receptors whereby the glutamate EC50 was shown to increase by Neto proteins [Neto1: 34-fold and Neto2: 7.5-fold (Palacios-Filardo et al., 2016) and Neto1/2: 10-30X (Fisher, 2015)]". It seems that values from Fisher's paper are backward. Please correct. 

(7) Page 9. Second paragraph. Spelling mistake when referring to Fig. 3G.

Thanks for pointing out the inadvertent errors; we have now corrected all of them.

(8) Figure 3: The title in Y axis overlaps with the figure. Please check.

We have corrected the error.

(9) Page 10: "In addition, K375/379/382H376-E mutant also exhibited a slowdown in the recovery (K375/379/382H376-E: 4.83 {plus minus} 0.31 s P=0.2774) (Figure 4C; Table 1)." Statistical analysis indicates this is not correct. Please tone down this statement. For example: "...mutant also exhibited a trend to a slowdown in the recovery although differences do not reach statistical significance".

Thanks. We have modified the statement as suggested.

(10) Page 11: "and a reduction was observed for K375/379/382H376-E receptors (1.17 {plus minus} 0.28 P=0.3733) compared to wild-type (Figure 4D; Table 1)." Same issue as the previous minor comment.

Thanks. We have modified the statement as suggested.

(11) Page 11: "We observed that mutants K368-E and K368/375/379/382H376-E, desensitize significantly slower in the presence of Neto1" This statement is not true for K368/375/379/382H376-E mutant. Please correct.

Thanks. We have modified the statement as suggested and specified the difference.

(12) Legend Figure 4. Colored asterisks are not clear in the figure. Please check.

Thanks. The reference to colored asterisks has been removed from the legend as they are not used.

(13) Representative data shown in Fig 5 sup.2A do not match very well with the final quantification shown in Fig 5A. Please check. Also, the authors state in the result section (page 10) that data shown in Fig. 5A indicate that "GluK1-1a modulation by Neto 1 is influenced by the splice residues". This could be true only for residue K368; however, this is not so obvious since the two mutants containing K368E are inconsistent. Please check and clarify.

Only representative traces are shown in Fig 5 sup 2 A. However, the quantification shown in Fig 5 A is from multiple cells. We have rechecked all the data and found it to be consistent. We have rewritten this section and modified it for better clarity.

(14) Figure 6-supplement 2: Please incorporate missing values of MW standards in panel B.

Thanks. We have modified the figure to include values for MW standards.

(15) It is not clear the rationale for showing construct C552Y C557V C575S in Fig. 6 sup.3, panel A. This mutant is not mentioned in the manuscript.

It has been mentioned in the methodology section under “Construct design for expression and purification of rat GluK1-1aEM”. It (C552Y C557V C576S) is one of the constructs used in optimizations that were checked for good protein yields. Based on FSEC protein profiles, we used C552Y, C557V (2X Cys mutant) as GluK1-1aEM, which is mentioned in the same section.

(16) Fig. 6 sup.4 Not clear what does mean w.r.c. Please specify in the legend.

With respect to (w. r. t.) has been specified in the manuscript.

(17) Suggestion to improve data presentation in Fig. 4D and Fig. 3 sup.1B: For easier comparison of IK/IG ratios, representative traces for kainate and glutamate in the same group could be shown using the same Y-scale.

It has been purposely shown with two different Y-scales due to the differences in peak amplitudes in the presence of glutamate or kainate. 

(18) Fig. 3 sup.1A: Based on the figure legend, horizontal bars representing the application of glutamate are not consistent with time scale bars. Please, check. In the same figure, panel B, the representative traces shown for GluK-1a-Neto1 are not consistent with IK/IG ratio shown in Fig. 3D.

Thanks, we have corrected the horizontal bars representing glutamate application. The representative traces shown for GluK-1a-Neto1 were rechecked and are consistent with the IK/IG ratio shown in Fig. 3D.

(19) I wonder if the authors could discuss the lack of Neto1 effect on the wild type Gluk1-2a channel, as proposed previously.

Sheng et al., 2015 showed that Neto1 enhances the desensitization onset of GluK1. However, it is unclear which GluK1 splice variants were used in that study. GluK1 has several splice variants, but in the present study, we specifically compared GluK1-1a and 2a. In our case, we did not observe the effect of Neto1 on wild-type GluK1-2a in either of the two techniques (whole cell and outside-out patch) we utilized for our study. However, as can be observed from our data, the GluK1-2a receptor alone shows a faster desensitization kinetics than the previous study (Copits et al., 2011). The differences could stem from different experimental conditions such as constructs, recording conditions used etc.

Copits BA, Robbins JS, Frausto S, Swanson GT. Synaptic targeting and functional modulation of GluK1 kainate receptors by the auxiliary neuropilin and tolloid-like (NETO) proteins. Journal of Neuroscience. 2011 May 18;31(20):7334-40.

Sheng N, Shi YS, Lomash RM, Roche KW, Nicoll RA. Neto auxiliary proteins control both the trafficking and biophysical properties of the kainate receptor GluK1. Elife. 2015 Dec 31;4:e11682. doi: 10.7554/eLife.11682. PMID: 26720915; PMCID: PMC4749551.

eLife assessment

This manuscript uses public datasets of myelodysplastic syndrome (MDS) patients to undertake a multi-omics analysis of clinical, genomic, and transcriptomic datasets. Useful findings are provided by way of interesting correlations of specific mutations with inflammation and differing clinical outcomes. The evidence is solid and interesting, and the manuscript is of substantive value to hematologists and clinical immunologists.

Reviewer #2 (Public Review):

Summary:

The authors performed a Multi-Omics Factor Analysis (MOFA) on analysis of two published MDS patient cohorts-1 from bone marrow mononuclear cells (BMMNCs) and CD34 cells (ref 17) and another from CD34+ cells (ref 15) --with three data modalities (clinical, genotype, and transcriptomics). Seven different views, including immune profile, inflammation/aging, Retrotransposon (RTE) expression, and cell- type composition, were derived from these modalities to attempt to identify the latent factors with significant impact on MDS prognosis.

SF3B1 was found to be the only mutation among 13 mutations in the BMMNC cohort that indicated a significant association with high inflammation. This trend was also observed to a lesser extent in the CD34+ cohort. The MOFA factor representing inflammation showed a good prognosis for MDS patients with high inflammation. In contrast, SRSF2 mutant cases showed a granulocyte-monocyte progenitor (GMP) pattern and high levels of senescence, immunosenescence, and malignant myeloid cells, consistent with their poor prognosis. Also, MOFA identified RTE expression as a risk factor for MDS. They proposed that this work showed the efficacy of their integrative approach to assess MDS prognostic risk that 'goes beyond all the scoring systems described thus far for MDS'.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews: 

Reviewer #1 (Public Review): 

In their manuscript, Gerlevik et al. performed an integrative analysis of clinical, genetic and transcriptomic data to identify MDS subgroups with distinct outcomes. The study was based on the building of an "immunoscore" and then combined with genotype and clinical data to analyze patient outcomes using multi-omics factor analysis. 

Strengths: Integrative analysis of RNA-seq, genotyping and clinical data 

Weaknesses: Validation of the bioinformatic pipeline is incomplete 

Major comments: 

(1) This study considered two RNA-seq data sets publicly available and generated in two distinct laboratories. Are they comparable in terms of RNA-seq technique: polyA versus rRNA depletion, paired-end sequencing, fragment length? 

We want to reemphasize that the main point of this study is not to compare the BMMNC with the HSPC cohort. These datasets are not comparable because they were

collected from different cell types, and we should not expect them to be matched. We just analysed them in parallel to check how much HSPCs contribute to the molecular signatures we see in BMMNC samples. However, we agree with the reviewer that similar RNA-seq experimental techniques should be employed to control for confounding factors. Here is the information that we found for HSPC and BMMNC RNA-seq studies:

HSPC RNA-seq cohort: Total RNA was extracted using TRIzol (Thermo Scientific), and Sequencing was performed on an Illumina HiSeq4000 with 100-bp paired-end reads.

BMMNC RNA-seq cohort: The RNA was extracted with TRIzol reagent (Thermo Scientific). RNA-sequencing libraries were prepared from poly(A)-selected RNA and were sequenced using Illumina HiSeq 2000 or 2500 platform with 100-bp paired-end reads. 

The only difference between the two cohorts is that one cohort includes total RNAs, whereas the other has polyA-selected RNAs. Since the gene set signatures use the expression of proteincoding genes, which all have polyA tails and are included in total RNA libraries, the analysis will not be affected by total vs. polyA-selected RNA-seq techniques. 

(2) Data quality control (figure 1): the authors must show in a graph whether the features (dimensions) of factor 1 were available for each BMMNC and CD34+ samples.  

By features of Factor 1, we think the reviewer means the features with high weights for Factor 1 in BMMNC and CD34+ samples. Figure 2c-d clearly illustrates the important features and their associations with Factor 1 for all samples in both cohorts. The samples are the columns of the two heatmaps.

(3) How to validate the importance of "immunoscore"? If GSEA of RNA-seq data was performed in the entire cohort, in the SF3B1-mutated samples or SRSF2-mutated samples (instead of patients having a high versus low level of factor 1 shown in Sup Fig. 4), what would be the ranking of Hallmarks or Reactome inflammatory terms among the others? 

Our GSEA analysis was an attempt to validate the importance of our identified factors. As described in the paper, Factor 1 represents a combination of immunology scores (or  “immunoscores”) in CD34+ cohort. Applying GSEA, we identified upregulation of inflammation related pathways, chemokines, and Neutrophils in patients having high (4th quartile) versus low (1st quartile) levels of Factor 1. Interestingly, sorting patients by Factor 1 resulted in similar pattern based on gene signature scores (Figure 2d).    

To show that Factor1 generated by MOFA is important and different from known MDS categories such as SF3B1 and SRSF2 mutants, we performed GSEA in SF3B1-mutated vs. SF3B1-WT samples and SRSF2-mutated vs. SRSF2-WT samples in the CD34+ cohort. As shown in Author response image 1, we did not see the upregulation of inflammation and interferon pathways in SF3B1 and SRSF2 mutant MDS.

Author response image 1.

GSEA showed no upregulation of inflammation and interferon pathways for SF3B1 and SRSF2 mutant in CD34+ cohort.  

(4) To decipher cell-type composition of BMMNC and CD34+ samples, the authors used van Galen's data (2019; supplementary table 3). Cell composition is expressed as the proportion of each cell population among the others. Surprisingly, the authors found that the promonocytelike score was increased in SF3B1-mutated samples and not in SRSF2-mutated samples, which are frequently co-mutated with TET2 and associated with a CMML-like phenotype. Is there a risk of bias if bone marrow subpopulations such as megakaryocytic-erythroid progenitors or early erythroid precursors are not considered? 

We thank the reviewer for their insightful comment about CMML and the high prevalence of SRSF2 mutation (> 45%) in CMML cases. Using single-cell RNA sequencing and high-parameter flow cytometry, Ferrall-Fairbanks et al. (DOI: 10.1158/2643-3230.BCD-21-0217) recently showed that CMML can be classified into three differentiation trajectories: monocytic, megakaryocyte-erythroid progenitor (MEP), and normal-like. One hallmark of monocytic-biased trajectory was the enrichment of inflammatory granulocyte–macrophage progenitor (GMP)-like cells, which we observed through our analysis for SRSF2 mutants (Figure 6a).

Unfortunately,  van Galen's data does not provide any gene set for MEP, and there is no singlecell RNA-seq atlas for MDS to employ to calculate the MEP score. Also, we compared the Promono-like and GMP-like gene sets from van Galen's data, and we could not find any overlap, meaning that Promono-like is not specific enough to capture the signatures coming from the more differentiated progenitors such as GMPs. Therefore, as described in the paper, we focused on GMP-like rather than Promono-like.

(5) Figures 2a and 2b indicated that the nature of retrotransposons identified in BMMNC and CD34+ was dicerent. ERVs were not detected in CD34+ cells. Are ERVs not reactivated in CD34+ cells? Is there a bias in the sequencing or bioinformatic method?  

As described above, the two cohorts' sequencing methods, read length, etc., are identical.

CD34+ RNA-seq is total RNA-seq that includes both polyA and non-polyA RTE transcripts.

Therefore, the chance of bias and missing RTE signatures in CD34+ cohort is very low. L1 and Alu, which are shared between the two cohorts, are the two RTE families that are still active and make new insertions in humans. Our interpretation is that ERV activation in BM is associated with immune cells. As shown by Au et al. (DOI: 10.1016/j.ccell.2021.10.001), several ERV loci had expression in purified immune cell subsets in renal cell carcinoma samples, potentially explaining ERV upregulation in tumours responding to treatment as those biopsies had increased tumour infiltration.

(6) What is the impact of factor 1 on survival? Is it dicerent between BMMNC and CD34+ cells considering the distinct composition of factor 1 in CD34+ and BMMNC? 

As shown in Table 1, Factor 1 in the BMMNC cohort is associated with overall survival (P-val < 0.05) when we did multivariate analysis but not univariate analysis. We did not observe any association between Factor 1 and event-free survival in the BMMNC cohort. Also, The 10 factors identified by MOFA in BM CD34+ cohort did not show any significance associated with MDS overall survival (Supplementary Table 5). 

(7) In Figure 1e, genotype contributed to the variance of in the CD34+ cell analyses more importantly than in the BMMNC. Because the patients are dicerent in the two cohorts, dicerences in the variance could be explained either by a greater variability of the type of mutations in CD34 or an increased frequency of poor prognosis mutations in CD34+ compared to BMMNC. The genotyping data must be shown.  

The genotype has already been reported in Supplementary Table 2. In fact, the number of inspected genes was much higher in the BMMNC cohort (17 genes) compared to the CD34+ cohort (3 genes). Therefore, we have more significant variability of the type of mutations in the BMMNC cohort compared to the CD34+ cohort. For the CD34+ cohort, we only had mutations for three spliceosome genes, where most cases (n=28) were SF3B1 mutants with good prognosis. We think that the result makes sense because the less genetic variability, the more homogenous groups and the more chance that one factor or a group of factors can explain the genetic variance.   

(8) Fig. 2a-b: Features with high weight are shown for each factor. For factor 9, features seemed to have a low weight (Fig. 1b and 1c). However, factor 9 was predictive of EFS and OS in the BMMNC cohort. What are the features driving the prognostic value of factor 9? 

As shown in Figure 3b, The main features are RTE expression from LTR:ERV1, SINE:MIR, and SINE:Alu family.  

(9) The authors also provided microarray analyses of CD34+ cell. It could be interesting to test more broadly the correlation between features identified by RNA-seq or microarrays. 

The microarray data did not come with any genetic information or clinical data except survival information. Therefore, we could not apply MOFA on Microarray data. However, we did generate gene signature scores from Microarray data and investigated the relationship between inflammatory chemokines and cytokines, and IFN-I signature scores with MDS survival (Figure 3c and 4c).    

(10) The authors should discuss the relevance of immunosenescence features in the context of SRSF2 mutation and extend the discussion to the interest of their pipeline for patient diagnosis and follow up under treatments. 

We have added the below text to the discussion:

Recent studies have shown that the expression of programmed death-ligand 1 (PD-L1) protein is significantly elevated in senescent cells (DOIs: 10.1128/mcb.00171-22, 10.1172/JCI156250, 10.1038/s41586-022-05388-4). Increased PD-L1 protein levels protect senescent cells from being cleared by cytotoxic immune cells that express the PD-1 checkpoint receptor. In fact, activation of the PD-1 receptor inhibits the cytotoxic capabilities of CD8 + T and NK cells, increasing immunosenescence.   

Notably, patients with MDS who possess particular somatic mutations, such as those in the TP53, ASXL1, SETBP1, TET2, SRSF2, and RUNX1 genes, have an increased propensity to react favourably to PD-1/PD-L1 inhibitors (DOIs: 10.1111/bjh.17689, https://doi.org/10.1182/blood2020-141100) confirming that many cellular and molecular mechanisms, known to promote cellular senescence, including alteration of splicing machinery, are crucial stimulators of the expression of PD-L1 protein. Interestingly, in our analysis, we also observed a correlation between the senescence gene signature score and the expression of the PD-L1 gene in CD34+ cells (Supplementary Figure 7), supporting the previous findings linking PD-L1 gene expression to cellular senescence.

The immunology and ageing features extracted from the MDS transcriptomic data used in our analysis pipeline can enhance the conventional risk-scoring systems for MDS by providing new insights into this disease, particularly in the context of inflammation and ageing. For some patients, the clinical and genetic features may remain relatively the same until follow-up. Still, the transcriptomic features might differ considerably from the baseline diagnosis, affecting the course of treatment.    

Reviewer #2 (Public Review): 

The authors performed a Multi-Omics Factor Analysis (MOFA) on analysis of two published MDS patient cohorts-1 from bone marrow mononuclear cells (BMMNCs) and CD34 cells (ref 17) and another from CD34+ cells (ref 15) --with three data modalities (clinical, genotype, and transcriptomics). Seven different views, including immune profile, inflammation/aging, Retrotransposon (RTE) expression, and cell-type composition, were derived from these modalities to attempt to identify the latent factors with significant impact on MDS prognosis. 

SF3B1 was found to be the only mutation among 13 mutations in the BMMNC cohort that indicated a significant association with high inflammation. This trend was also observed to a lesser extent in the CD34+ cohort. The MOFA factor representing inflammation showed a good prognosis for MDS patients with high inflammation. In contrast, SRSF2 mutant cases showed a granulocyte-monocyte progenitor (GMP) pattern and high levels of senescence, immunosenescence, and malignant myeloid cells, consistent with their poor prognosis. Also, MOFA identified RTE expression as a risk factor for MDS. They proposed that this work showed the efficacy of their integrative approach to assess MDS prognostic risk that 'goes beyond all the scoring systems described thus far for MDS'. 

Several issues need clarification and response: 

(1) The authors do not provide adequate known clinical and molecular information which demonstrates prognostic risk of their sample cohorts in order to determine whether their data and approach 'goes 'beyond all the scoring systems described thus far for MDS'. For example, what data have the authors that their features provide prognostic data independent of the prior known factors related to prognosis (eg, marrow blasts, mutational, cytogenetic features, ring sideroblasts, IPSS-R, IPSS-M, MDA-SS)? 

We agree with the reviewer that we did not generate a new cumulative risk score and compare it with the conventional risk scores for MDS. However, we identified individual MOFA factors, which are risk or protective factors for MDS, based on survival analysis in the BMMNC cohort. One reason that we did not generate our independent, cumulative score and compare it with other scores was that we did not receive any conventional risk score for the BMMNC cohort. However, we had access to all the clinical and genetic variables from the BMMNC cohort (except for three patients) that were required to calculate IPSS-R; hence, we calculated the IPSS-R in our resubmission for the BMMNC cohort. We made three IPSS-R risk categories by combining low and very low as low risk, and high and very high as high risk, and keeping intermediate as intermediate risk. Our survival analysis of these three categories showed a clear match between IPSS-R score and MDS survival (Author response image 2a).

We then investigated the relationship between factors 2, 4, and 9 from MOFA with three IPSS-R risk groups.  Integration of IPSS-R risk groups with factor values confirmed the finding in the manuscript that Factors 4 and 9 generally exert a protective influence over the MDS risk, whilst higher levels of Factor 2 predict a high-risk MDS (Author response image 2b). However, we see so many outliers in all three factors, indicating that some patients were assigned to the wrong IPSS-R categories because IPSS-R calculation is based on clinical and genetic variables and does not include the transcriptomics data for coding and non-coding genomic regions. 

Author response image 2.

Comparison of IPSS-R risk categories and MOFA risk and protective factors.

(2) A major issue in analyzing this paper relates to the specific patient composition from whom the samples and data were obtained. The cells from the Shiozawa paper (ref 17) is comprised of a substantial number of CMML patients. Thus, what evidence have the authors that much of the data from the BMMNCs from these patients and mutant SRSF2 related predominantly to their monocytic dicerentiation state?  

We thank the reviewer for the insightful comment about the monocytic differentiation state of CMML and SRSF2 mutant cases. The BMMNC cohort has 11 CMML and 17 SRSF2 mutant cases, of which six are shared between the two groups. We have divided the patients into four groups: CMML only, SRSF2 mutant only, CCML and SRSF2 mutant, and others. We have generated boxplots for all cellular composition gene signature scores for these groups and compared the scores between these groups. As explained above, Ferrall-Fairbanks et al. (DOI: 10.1158/2643-3230.BCD-21-0217) recently showed that CMML can be classified into three differentiation trajectories: monocytic, megakaryocyte-erythroid progenitor (MEP), and normal-like. One hallmark of monocytic-biased trajectory was the enrichment of inflammatory granulocyte–macrophage progenitor (GMP)-like cells, which we observed through our analysis for the CMML cases with SRSF2 mutation (Author response image 3.).

Author response image 3.

Cellular composition gene signature scores for CMML and SRSF2 mutant versus other cases. CMML cases with SRSF2 mutation show a significant higher level of GMP and GMP-like scores compared to other MDS cases.  

(3) In addition, as the majority of patients in the Shiozawa paper have ring sideroblasts (n=59), thus potentially skewing the data toward consideration mainly of these patients, for whom better outcomes are well known.  

We disagree with the reviewer. We used 94 BMMNC samples from Shiozawa’s paper, of which 19 cases had Refractory Anemia with Ring Sideroblasts (RARS), 4 cases had Refractory Anemia with Ring Sideroblasts and thrombocytosis (RARS-T), and 5 cases had Refractory cytopenia with multilineage dysplasia and ring sideroblasts (RCMD-RS). In total, we had 28 cases (~30%) with Ring Sideroblasts (RS), which are not large enough to skew the data.

(4) Further, regarding this patient subset, what evidence have the authors that the importance of the SF3B1 mutation was merely related to the preponderance of sideroblastic patients from whom the samples were analyzed? 

We had 34 SF3B1 mutant cases, of which 25 had Ring Sideroblasts (RS). The total number of cases with RS in the BMMNC cohort was 28. Therefore, the BMMNC cohort is not an RSdominant cohort, and RS cases did not include all SF3B1 mutants. Furthermore, it was recently shown by Ochi et al. (DOI: 10.1038/s41598-022-18921-2) that RS is a consequence of SF3B1K700E mutation, and it is not a cause to affect the SF3B1 importance.

(5) An Erratum was reported for the Shiozawa paper (Shiozawa Y, Malcovati L, Gallì A, et al. Gene expression and risk of leukemic transformation in myelodysplasia. Blood. 2018 Aug 23;132(8):869-875. doi: 10.1182/blood-2018-07-863134) that resulted from a coding error in the construction of the logistic regression model for subgroup prediction based on the gene expression profiles of BMMNCs. This coding error was identified after the publication of the article. The authors should indicate the ecect this error may have had on the data they now report.  

Thank you for bringing this important issue to our attention. The error resulted from a mistake in the construction of the logistic regression model for subgroup prediction based on the gene expression profiles of BMMNCs. However, this issue does not affect our result because we analysed the expression data from scratch and generated our own gene signature scores. Also, the error has no impact on the genetics and clinical information that we received from the authors.

(6) What information have the authors as to whether the dicering RTE findings were not predominantly related to the dicerentiation state of the cell population analyzed (ie higher in BM MNCs vs CD34, Fig 1)? What control data have the authors regarding these values from normal (non-malignant) cell populations? 

As described above, L1 and Alu, the two RTE families shared between the two cohorts, are still active and make new insertions in humans (Figure 2.a-b). Our interpretation is that ERV activation in BM is associated with immune cells. This interpretation is further supported by the findings of Au et al. (DOI: 10.1016/j.ccell.2021.10.001), where several ERV loci had expression in purified immune cell subsets in renal cell carcinoma samples. 

Unfortunately, none of these two cohorts had normal (non-malignant) cell populations. We think that the MOFA unbiased way of modelling the heterogeneity is su@icient to capture the RTE derepressed phenotype of a subset of MDS cases compared to others, and we do not need normal cases to further support the finding. 

(7) The statement in the Discussion regarding the ecects of SRSF2 mutation is speculative and should be avoided. Many other somatic gene mutations have known stronger ecects on prognosis for MDS. 

One aim of this study is to identify specific immune signatures associated with SRSF2 and SF3B1 mutations, which are highly prevalent in MDS. Although other mutations, such as TP53, may have a stronger correlation with poor survival, numerous studies have demonstrated a clear link between SRSF2 mutations and poor prognosis.

eLife assessment

This important study reports a high-resolution cryoEM structure of the supercomplex between photosystem I (PSI) and fucoxanthin chlorophyll a/c-binding proteins (FCPs) from the model diatom Thalassiosira pseudonana CCMP1335, with subunits, protein:protein interactions and pigments not previously seen in other diatoms or red/green photosynthetic lineages. Combining structural, sequence, and phylogenetic analyses, the authors provide convincing evidence of conserved motifs crucial for the binding of FCPs, leading to interesting speculation about the mechanisms governing the assembly of PSI-FCP supercomplexes in diatoms and their implications for related PSI-LHC supercomplexes in plants. The findings set the basis for functional experiments that will further advance the fields of photosynthesis, bioenergy, ocean biogeochemistry, and understanding of evolutionary relationships between photosynthetic organisms.

Reviewer #1 (Public Review):<br /> The authors present the cryo-EM structure of of PSI-fucoxanthin chlorophyll a/c-binding proteins (FCPs) supercomplex from the diatom Thalassiosira pseudonana CCMP1335 at a global resolution of 2.3 Å. This exceptional resolution allows the authors to construct a near-atomic model of the entire supercomplex and elucidate the molecular details of FCPs arrangement. The high-resolution structure reveals subunits not previously identified in earlier reconstructions and models, as well as sequence analysis of PSI-FCPIs from other diatoms and red algae. Additionally, the authors use their model in conjunction with a phylogenetic analysis to compare and contrast the structural features of the T. pseudonana supercomplex with those of Chaetoceros gracilis, uncovering key structural features that contribute to the efficiency of light energy conversion in diatoms.

The study employs the advanced technique of single particle cryo-electron microscopy to visualize the complex architecture of the PSI supercomplex at near-atomic resolution and analyze the specific roles of FCPs in enhancing photosynthetic performance in diatoms.

Overall, the approach and data are both compelling and of high quality. The paper is well written and will be of wide interest for comprehending the molecular mechanisms of photosynthesis in diatoms. This work provides valuable insights for applications in bioenergy, environmental conservation, plant physiology, and membrane protein structural biology.

Reviewer #2 (Public Review):

Summary:

This manuscript elucidated the cryo-electron microscopic structure of a PSI supercomplex incorporating fucoxanthin chlorophyll a/c-binding proteins (FCPs), designated as PSI-FCPI, isolated from the diatom Thalassiosira pseudonana CCMP1335. Combining structural, sequence, and phylogenetic analyses, the authors provided solid evidence to reveal the evolutionary conservation of protein motifs crucial for the selective binding of individual FCPI subunits and provided valuable information about the molecular mechanisms governing the assembly and selective binding of FCPIs in diatoms.

Strengths:

The manuscript is well-written and presented clearly as well as consistently. The supplemental figures are also of high quality.

Weaknesses:

Only minor comments (provided in recommendations for authors) to help improve the manuscript.

Reviewer #3 (Public Review):

Summary:

Understanding the structure and function of the photosynthetic machinery is crucial for grasping its mode of action. Photosystem I (PSI) plays a vital role in light-driven electron transfer, which is essential for generating cellular reducing power. A primary strategy to mitigate light and environmental stresses involves incorporating peripheral light-harvesting proteins. Among various lineages, the number of LHCIs and their protein and pigment compositions differ significantly in PSI-LHCI structures. However, it is still unclear how LHCIs recognize their specific binding sites in the PSI core. This study aims to address this question by obtaining a high-resolution structure of the PSI supercomplex, including fucoxanthin chlorophyll a/c-binding proteins (FCPs), referred to as PSI-FCPI, isolated from the diatom Thalassiosira pseudonana. Through structural and sequence analyses, distinct protein-protein interactions are identified at the interfaces between FCPI and PSI subunits, as well as among FCPI subunits themselves.

Strengths:

The primary strength of this work lies in its superb isolation and structural determination, followed by clear discussion and conclusions. However, the interactions among the protein complexes and their relevance in formulating general rules are not definitively established. While efficiency is a crucial aspect, preventing damage is equally important, and currently, we cannot infer this from the provided structures.

Weaknesses:

The interactions among the protein complexes and their relevance in formulating general rules are not definitively established. While efficiency is a crucial aspect, preventing damage is equally important, and currently, we cannot infer this from the provided structures.

eLife assessment

This valuable study by Wu et al presents data on bacterial cell organization, with the goal of demonstrating that the two structures that account for bacterial motility - the chemotaxis complex and the flagella - colocalize to the same pole in Pseudomonas aeruginosa cells and expose the regulation underlying their spatial organization and functioning. The subject is of importance and the manuscript is well written. However, the work is incomplete and the conclusions are too strong for the presented data. This manuscript will be of interest to cell biologists, mainly those studying bacteria, but not only, if the evidence is substantiated, the assumptions clarified, and the novelty is made clear during the revision process.

Reviewer #1 (Public Review):

Summary:

The study by Wu et al presents interesting data on bacterial cell organization, a field that is progressing now, mainly due to the advances in microscopy. Based mainly on fluorescence microscopy images, the authors aim to demonstrate that the two structures that account for bacterial motility, the chemotaxis complex and the flagella, colocalize to the same pole in Pseudomonas aeruginosa cells and to expose the regulation underlying their spatial organization and functioning.

Strengths:

The subject is of importance.

Weaknesses:

The conclusions are too strong for the presented data. The lack of statistical analysis makes this paper incomplete. The novelty of the findings is not clear.

Major issues:

(1) The novelty is in question since in the Abstract the authors highlight their main finding, which is that both the chemotaxis complex and the flagella localize to the same pole, as surprising. However, in the Introduction they state that "pathway-related receptors that mediate chemotaxis, as well as the flagellum are localized at the same cell pole17,18". I am not a pseudomonas researcher and from my short glance at these references, I could not tell whether they report colocalization of the two structures to the same pole. However, I trust the authors that they know the literature on the localization of the chemotaxis complex and flagella in their organism. See also major issue number 5 on the novelty regarding the involvement of c-di-GMP.

(2) Statistics for the microscopy images, on which most conclusions in this manuscript are based, are completely missing. Given that most micrographs present one or very few cells, together with the fact that almost all conclusions depend on whether certain macromolecules are at one or two poles and whether different complexes are in the same pole, proper statistics, based on hundreds of cells in several fields, are absolutely required. Without this information, the results are anecdotal and do not support the conclusions. Due to the importance of statistics for this manuscript, strict statistical tests should be used and reported. Moreover, representative large fields with many cells should be added as supportive information.

The problem is more pronounced when the authors make strong statements, as in lines 157-158: "The results revealed that the chemoreceptor arrays no longer grow robustly at the cell pole (Figure 2A)". Looking at the seven cells shown in Figure 2A, five of them show polar localization of the chemoreceptors. The question is then: what is the percentage of cells that show precise polar, near-polar, or mid cell localization (the three patterns shown here) in the mutant and in the wild type? Since I know that these three patterns can also be observed in WT cells, what counts is the difference, and whether it is statistically significant.

Even for the graphs shown in Figures 3C and 3D, where the proportion of cells with obvious chemoreceptor arrays and absolute fluorescence brightness of the chemosensory array are shown, respectively, the questions that arise are: for how many individual cells these values hold and what is the significance of the difference between each two strains?

(3) The authors conclude that "Motor structural integrity is a prerequisite for chemoreceptor self-assembly" based on the reduction in cells with chemoreceptor clusters in mutants deleted for flagellar genes, despite the proper polar localization of the chemotaxis protein CheY. They show that the level of CheY in the WT and the mutant strains is similar, based on Western blot, which in my opinion is over-exposed. "To ascertain whether it is motor integrity rather than functionality that influences the efficiency of chemosensory array assembly", they constructed a mutant deleted for the flagella stator and found that the motor is stalled while CheY behaves like in WT cells. The authors further "quantified the proportion of cells with receptor clusters and the absolute fluorescence intensity of individual clusters (Figures 3C-D)". While Figure 3DC suggests that, indeed, the flagella mutants show fewer cells with a chemotaxis complex, Figure 3D suggests that the differences in fluorescence intensity are not statistically significant.

Since it is obvious that the regulation of both structures' production and localization is codependent, I think that it takes more than a Western blot to make such a decision.

(4) I wonder why the authors chose to label CheY, which is the only component of the chemotaxis complex that shuttles back and forth to the base of the flagella. In any case, I think that they should strengthen their results by repeating some key experiments with labeled CheW or CheA.

(5) The last section of the results is very problematic, regarding the rationale, the conclusions, and the novelty. As far as the rationale is concerned, I do not understand why the authors assume that "a spatial separation between the chemoreceptors and flagellar motors should not significantly impact the temporal comparison in bacterial chemotaxis". Is there any proof for that? More surprising for me was to read that "The signal transduction pathways in E. coli are relatively simple, and the chemotaxis response regulator CheY-P affects only the regulation of motor switching". There are degrees of complexity among signal transduction pathways in E. coli, but the chemotaxis seems to be ranked at the top. CheY is part of the adaptation. Perfect adaptation, as many other issues related to the chemotaxis pathway, which include the wide dynamic range, the robustness, the sensitivity, and the signal amplification (gain), are still largely unexplained. Hence, such assumptions are not justified.

More perplexing is the novelty of the authors' documentation of the effect of the chemotaxis proteins on the c-di-GMP level. In 2013, Kulasekara et al. published a paper in eLife entitled "c-di-GMP heterogeneity is generated by the chemotaxis machinery to regulate flagellar motility". In the same year, Kulasekara published a paper entitled "Insight into a Mechanism Generating Cyclic di-GMP Heterogeneity in Pseudomonas aeruginosa". The authors did not cite these works and I wonder why.

(6) Throughout the manuscript, the authors refer to foci of fluorescent CheY as "chemoreceptor arrays". If anything, these foci signify the chemotaxis complex, not the membrane-traversing chemoreceptors.

Conclusions:

The manuscript addresses an interesting subject and contains interesting, but incomplete, data.

Reviewer #2 (Public Review):

Summary:

Here, the authors studied the molecular mechanisms by which the chemoreceptor cluster and flagella motor of Pseudomonas aeruginosa (PA) are spatially organized in the cell. They argue that FlhF is involved in localizing the receptors-motor to the cell pole, and even without FlhF, the two are colocalized. FlhF is known to cause the motor to localize to the pole in a different bacterial species, Vibrio cholera, but it is not involved in receptor localization in that bacterium. Finally, the authors argue that the functional reason for this colocalization is to insulate chemotactic signaling from other signaling pathways, such as cyclic-di-GMP signaling.

Strengths:

The experiments and data look to be high-quality.

Weaknesses:

However, the interpretations and conclusions drawn from the experimental observations are not fully justified in my opinion.

I see two main issues with the evidence provided for the authors' claims.

(1) Assumptions about receptor localization:

The authors rely on YFP-tagged CheY to identify the location of the receptor cluster, but CheY is a diffusible cytoplasmic protein. In E. coli, CheY has been shown to localize at the receptor cluster, but the evidence for this in PA is less strong. The authors refer to a paper by Guvener et al 2006, which showed that CheY localizes to a cell pole, and CheA (a receptor cluster protein) also localizes to a pole, but my understanding is that colocalization of CheY and CheA was not shown. My concern is that CheY could instead localize to the motor in PA, say by binding FliM. This "null model" would explain the authors' observations, without colocalization of the receptors and motor.

Verifying that CheY and CheA are colocalized in PA would be a very helpful experiment to address this weakness.

(2) Argument for the functional importance of receptor-motor colocalization at the pole:

The authors argue that colocalization of the receptors and motors at the pole is important because it could keep phosphorylated CheY, CheY-p, restricted to a small region of the cell, preventing crosstalk with other signaling pathways. Their evidence for this is that overexpressing CheY leads to higher intracellular cdG levels and cell aggregation.

Say that the receptors and motors are colocalized at the pole. In E. coli, CheY-p rapidly diffuses through the cell. What would prevent this from occurring in PA, even with colocalization?

Elevating CheY concentration may increase the concentration of CheY-p in the cell, but might also stress the cells in other unexpected ways. It is not so clear from this experiment that elevated CheY-p throughout the cell is the reason that they aggregate, or that this outcome is avoided by colocalizing the receptors and motor at the same pole.

If localization of the receptor array and motor at one pole were important for keeping CheY-p levels low at the opposite pole, then we should expect cells in which the receptors and motor are not at the pole to have higher CheY-p at the opposite pole. According to the authors' argument, it seems like this should cause elevated cdG levels and aggregation in the delta flhF mutants with wild-type levels of CheY. But it does not look like this happened.

Instead of varying CheY expression, the authors could test their hypothesis that receptor-motor colocalization at the pole is important for preventing crosstalk by measuring cdG levels in the flhF mutant, in which the motor (and maybe the receptor cluster) are no longer localized in the cell pole.

Reviewer #3 (Public Review):

Summary:

The authors investigated the assembly and polar localization of the chemosensory cluster in P. aeruginosa. They discovered that a certain protein (FlhF) is required for the polar localization of the chemosensory cluster while a fully-assembled motor is necessary for the assembly of the cluster. They found that flagella and chemosensory clusters always co-localize in the cell; either at the cell pole in wild-type cells or randomly-located in the cell in FlhF mutant cells. They hypothesize that this co-localization is required to keep the level of another protein (CheY-P), which controls motor switching, at low levels as the presence of high levels of this protein (if the flagella and chemosensory clusters were not co-localized) is associated with high-levels of c-di-GMP and cell aggregations.

Strengths:

The manuscript is clearly written and straightforward. The authors applied multiple techniques to study the bacterial motility system including fluorescence light microscopy and gene editing. In general, the work enhances our understanding of the subtlety of interaction between the chemosensory cluster and the flagellar motor to regulate cell motility.

Weaknesses:

The major weakness in this paper is that the authors never discussed how the flagellar gene expression is controlled in P. aeruginosa. For example, in E. coli there is a transcriptional hierarchy for the flagellar genes (early, middle, and late genes, see Chilcott and Hughes, 2000). Similarly, Campylobacter and Helicobacter have a different regulatory cascade for their flagellar genes (See Lertsethtakarn, Ottemann, and Hendrixson, 2011). How does the expression of flagellar genes in P. aeruginosa compare to other species? How many classes are there for these genes? Is there a hierarchy in their expression and how does this affect the results of the FliF and FliG mutants? In other words, if FliF and FliG are in class I (as in E. coli) then their absence might affect the expression of other later flagellar genes in subsequent classes (i.e., chemosensory genes). Also, in both FliF and FliG mutants no assembly intermediates of the flagellar motor are present in the cell as FliG is required for the assembly of FliF (see Hiroyuki Terashima et al. 2020, Kaplan et al. 2019, Kaplan et al. 2022). It could be argued that when the motor is not assembled then this will affect the expression of the other genes (e.g., those of the chemosensory cluster) which might play a role in the decreased level of chemosensory clusters the authors find in these mutants.

Reviewer #3 (Public Review):

Summary:<br /> In this study, Davies and Plate set out to discover conserved host interactors of coronavirus non-structural proteins (Nsp). They used 293T cells to ectopically express flag-tagged Nsp2 and Nsp4 from five human and mouse coronaviruses, including SARS-CoV-1 and 2, and analyzed their interaction with host proteins by affinity purification mass-spectrometry (AP-MS). To confirm whether such interactors play a role in coronavirus infection, the authors measured the effects of individual knockdowns on replication of murine hepatitis virus (MHV) in mouse Delayed Brain Tumor cells. Using this approach, they identified a previously undescribed interactor of Nsp2, Malectin (Mlec), which is involved in glycoprotein processing and shows a potent pro-viral function in both MHV and SARS-CoV-2. Although the authors were unable to confirm this interaction in MHV-infected cells, they show that infection remodels many other Mlec interactions, recruiting it to the ER complex that catalyzes protein glycosylation (OST). Mlec knockdown reduced viral RNA and protein levels during MHV infection, although such effects were not limited to specific viral proteins. However, knockdown reduced the levels of five viral glycopeptides that map to Spike protein, suggesting it may be affected by Mlec.

Strengths:<br /> This is an elegant study that uses a state-of-the-art quantitative proteomic approach to identify host proteins that play critical roles in viral infection. Instead of focusing on a single protein from a single virus, it compares the interactomes of two viral proteins from five related viruses, generating a high confidence dataset. The functional follow-ups using multiple live and reporter viruses, including MHV and CoV2 variants, convincingly depict a pro-viral role for Mlec, a protein not previously implicated in coronavirus biology.

Weaknesses:<br /> Although a commonly used approach, AP-MS of ectopically expressed viral proteins may not accurately capture infection-related interactions. The authors observed Mlec-Nsp2 interactions in transfected 293T cells (1C) but were unable to reproduce those in mouse cells infected with MHV (3C). EIF4E2/GIGYF2, two bonafide interactors of CoV2 Nsp2 from previous studies, are listed as depleted compared to negative controls (S1D). Most other CoV2 Nsp2 interactors are also depleted by the same analysis (S1D). Previously reported MERS Nsp2 interactors, including ASCC1 and TCF25, are also not detected (S1D). Furthermore, although GIGYF2 was not identified as an interactor of MHV Nsp2/4 in human cells (S1D), its knockdown in mouse cells reduced MHV titers about 1000 fold (S4). The authors should attempt to explain these discrepancies.

More importantly, the authors were unable to establish a direct link between Mlec and the biogenesis of any viral or host proteins, by mass-spectrometry or otherwise. Although it is clear that Mlec promotes coronavirus infection, the mechanism remains unclear. Its knockdown does not affect the proteome composition of uninfected cells (S15B), suggesting it is not required for proteome maintenance under normal conditions. The only viral glycopeptides detected during MHV infection originated from Spike (5D), although other viral proteins are also known to be glycosylated. Cells depleted for Mlec produce ~4-fold less Spike protein (4E) but no more than 2-fold less glycosylated spike peptides (5D), compounding the interpretation of Mlec effects on viral protein biogenesis. Furthermore, Spike is not essential for the pro-viral role of Mlec, given that Mlec knockdown reduces replication of SARS-CoV-2 replicons that express all viral proteins except for Spike (6A/B).

Any of the observed effects on viral protein levels could be secondary to multiple other processes. Interventions that delay infection for any reason could lead to an imbalance of viral protein levels because Spike and other structural proteins are produced at a much higher rate than non-structural proteins due to the higher abundance of their cognate subgenomic RNAs. Similarly, the observation that Mlec depletion attenuates MHV-mediated changes to the host proteome (S15C/D) can also be attributed to indirect effects on viral replication, regardless of glycoprotein processing. In the discussion, the authors acknowledge that Mlec may indirectly affect infection through modulation of replication complex formation or ER stress, but do not offer any supporting evidence. Interestingly, plant homologs of Mlec are implicated in innate immunity, favoring a more global role for Mlec in mammalian coronavirus infections.

Finally, the observation that both Nsp2 (3C) and Mlec (3E/F) are recruited to the OST complex during MHV infection neither support nor refute any of these alternate hypotheses, given that Mlec is known to interact with OST in uninfected cells and that Nsp2 may interact with OST as part of the full length unprocessed Orf1a, as it co-translationally translocates into the ER.

Therefore, the main claims about the role of Mlec in coronavirus protein biogenesis are only partially supported.

eLife assessment

This is a valuable study that utilizes proteomic and genetic approaches to identify the glycoprotein quality control factor malectin as a pro-viral host protein involved in the replication of coronavirus. The evidence supporting this conclusion is solid, although additional insight into the mechanistic basis of malectin-mediated viral replication would further strengthen this study. This work will be of interest to cell biologists studying the molecular mechanisms of glycoprotein quality control and virologists studying the host-pathogen interactions.

Reviewer #1 (Public Review):

In this manuscript, the authors employ a combined proteomic and genetic approach to identify the glycoprotein QC factor malectin as an important protein involved in promoting coronavirus infection. Using proteomic approaches, they show that the non-structural protein NSP2 and malectin interact in the absence of viral infection, but not in the presence of viral infection. However, both NSP2 and malectin engage the OST complex during viral infection, with malectin also showing reduced interactions with other glycoprotein QC proteins. Malectin KD reduce replication of coronaviruses, including SARS-COV2. Collectively, these results identify Malectin as a glycoprotein QC protein involved in regulating coronavirus replication that could potentially be targeted to mitigate coronavirus replication.

Overall, the experiments described appear well performed and the interpretations generally reflect the results. Moreover, this work identifies Malectin as an important pro-viral protein whose activity could potentially be therapeutically targeted for the broad treatment of coronavirus infection. However, there are some weaknesses in the work that, if addressed, would improve the impact of the manuscript.

Notably, the mechanism by which malectin regulates viral replication is not well described. It is clear from the work that malectin is a pro-viral protein in the work presented, but the mechanistic basis of this activity is not pursued. Some potential mechanisms are proposed in the discussion, but the manuscript would be strengthened if additional insight was included. For example, does the UPR activated to higher levels in infected cells depleted of malectin? Do glycosylation patterns of viral (or non-viral) proteins change in malectin-depleted cells? Additional insight into this specific question would significantly improve the manuscript.

Further, the evidence for increased interactions between OST and malectin during viral infection is fairly weak, despite being a major talking point throughout the manuscript. The reduced interactions between malectin and other glycoproteostasis QC factors is evident, but the increased interactions with OST are not well supported. I'd recommend backing off on this point throughout the text, instead, continuing to highlight the reduced interactions.

I was also curious as to why non-structural proteins, nsp2 and nsp4, showed robust interactions with host proteins localized to both the ER and mitochondria? Do these proteins localize to different organelles or do these interactions reflect some other type of dysregulation? It would be useful to provide a bit of speculation on this point.

Again, the overall identification of malectin as a pro-viral protein involved in the replication of multiple different coronaviruses is interesting and important, but additional insights into the mechanism of this activity would strengthen the overall impact of this work.

Reviewer #2 (Public Review):

Summary:<br /> A strong case is presented to establish that the endoplasmic reticulum carbohydrate binding protein malectin is an important factor for coronavirus propagation. Malectin was identified as a coronavirus nsp2 protein interactor using quantitative proteomics and its importance in the viral life cycle was supported by using a functional genetic screen and viral assays. Malectin binds diglucosylated proteins, an early glycoform thought to transiently exist on nascent chains shortly after translation and translocation; yet a role for malectin has previously been proposed in later quality control decisions and degradation targeting. These two observations have been difficult to reconcile temporally. In agreement with results from the Locher lab, the malectin-interactome shown here includes a number of subunits of the oligosaccharyltransferase complex (OST). These results place malectin in close proximity to both the co-translational (STT3A or OST-A) and post-translational (STT3B or OST-B) complexes. It follows that malectin knockdown was associated with coronavirus Spike protein hypoglycosylation.

Strengths:<br /> Strengths include using multiple viruses to identify interactors of nsp2 and quantitative proteomics along with multiple viral assays to monitor the viral life cycle.

Weaknesses:<br /> Malectin knockdown was shown to be associated with Spike protein hypoglycosylation. This was further supported by malectin interactions with the OSTs. However, no specific role of malectin in glycosylation was discussed or proposed.

Given the likelihood that malectin plays a role in the glycosylation of heavily glycosylated proteins like Spike, it is unfortunate that only 5 glycosites on Spike were identified using the MS deamidation assay when Spike has a large number of glycans (~22 sites). The mass spec data set would also include endogenous proteins. Were any heavily glycosylated endogenous proteins hypoglycosylated in the MS analysis in Fig 5D?

The inclusion of the nsp4 interactome and its partial characterization is a distraction from the storyline that focuses on malectin and nsp2.

Author response:

Public Reviews:

Reviewer #1 (Public Review):

In this manuscript, the authors employ a combined proteomic and genetic approach to identify the glycoprotein QC factor malectin as an important protein involved in promoting coronavirus infection. Using proteomic approaches, they show that the non-structural protein NSP2 and malectin interact in the absence of viral infection, but not in the presence of viral infection. However, both NSP2 and malectin engage the OST complex during viral infection, with malectin also showing reduced interactions with other glycoprotein QC proteins. Malectin KD reduce replication of coronaviruses, including SARS-COV2. Collectively, these results identify Malectin as a glycoprotein QC protein involved in regulating coronavirus replication that could potentially be targeted to mitigate coronavirus replication.

Overall, the experiments described appear well performed and the interpretations generally reflect the results. Moreover, this work identifies Malectin as an important pro-viral protein whose activity could potentially be therapeutically targeted for the broad treatment of coronavirus infection. However, there are some weaknesses in the work that, if addressed, would improve the impact of the manuscript.

Notably, the mechanism by which malectin regulates viral replication is not well described. It is clear from the work that malectin is a pro-viral protein in the work presented, but the mechanistic basis of this activity is not pursued. Some potential mechanisms are proposed in the discussion, but the manuscript would be strengthened if additional insight was included. For example, does the UPR activated to higher levels in infected cells depleted of malectin? Do glycosylation patterns of viral (or non-viral) proteins change in malectin-depleted cells? Additional insight into this specific question would significantly improve the manuscript.

We concur with the reviewer that the mechanism by which Malectin regulates viral replication remains unclear. It will be worth pursuing the molecular mechanisms underlying this phenotype in future studies. Our existing proteomics data sets can potentially offer additional insight into the questions posed here. Namely, we plan to analyze levels of protein markers of the UPR and other ER stress pathways in infected cells depleted of Malectin in our existing global proteomics data set. In addition, we will attempt to compare glycosylation patterns of endogenous proteins in Malectin-depleted cells. One caveat to this will be that it may be difficult to differentiate between spontaneous chemical deamidation and enzymatic PNGase F mediated deamidation.

Further, the evidence for increased interactions between OST and malectin during viral infection is fairly weak, despite being a major talking point throughout the manuscript. The reduced interactions between malectin and other glycoproteostasis QC factors is evident, but the increased interactions with OST are not well supported. I'd recommend backing off on this point throughout the text, instead, continuing to highlight the reduced interactions.

We note that the fold change increase of OST interactions with malectin are small compared to the fold change decrease of other glycoproteostasis factors. If this modest increase is consistent across replicates, we believe this bolsters the claim that it is a noteworthy change. However, if not, we can modify the text as suggested to emphasize the reduced interactions.

I was also curious as to why non-structural proteins, nsp2 and nsp4, showed robust interactions with host proteins localized to both the ER and mitochondria? Do these proteins localize to different organelles or do these interactions reflect some other type of dysregulation? It would be useful to provide a bit of speculation on this point.

We also find these ER and mitochondrial protein interactions curious, which we initially reported on (Davies, Almasy et al. 2020 ACS Infectious Diseases). In this prior report, we found that when expressed in HEK293T cells, SARS-CoV-2 nsp2 and nsp4 have partial localization to mitochondrial-associated ER membranes (MAMs), as determined by subcellular fractionation. Given that malectin has also been shown to have MAMs localization (Carreras-Sureda, et al. 2019 Nature Cell Biology), we can insert some speculation on this in the Discussion section.

Again, the overall identification of malectin as a pro-viral protein involved in the replication of multiple different coronaviruses is interesting and important, but additional insights into the mechanism of this activity would strengthen the overall impact of this work.

Reviewer #2 (Public Review):

Summary:

A strong case is presented to establish that the endoplasmic reticulum carbohydrate binding protein malectin is an important factor for coronavirus propagation. Malectin was identified as a coronavirus nsp2 protein interactor using quantitative proteomics and its importance in the viral life cycle was supported by using a functional genetic screen and viral assays. Malectin binds diglucosylated proteins, an early glycoform thought to transiently exist on nascent chains shortly after translation and translocation; yet a role for malectin has previously been proposed in later quality control decisions and degradation targeting. These two observations have been difficult to reconcile temporally. In agreement with results from the Locher lab, the malectin-interactome shown here includes a number of subunits of the oligosaccharyltransferase complex (OST). These results place malectin in close proximity to both the co-translational (STT3A or OST-A) and post-translational (STT3B or OST-B) complexes. It follows that malectin knockdown was associated with coronavirus Spike protein hypoglycosylation.

Strengths:

Strengths include using multiple viruses to identify interactors of nsp2 and quantitative proteomics along with

multiple viral assays to monitor the viral life cycle.

Weaknesses:

Malectin knockdown was shown to be associated with Spike protein hypoglycosylation. This was further supported by malectin interactions with the OSTs. However, no specific role of malectin in glycosylation was discussed or proposed.

We will emphasize our hypotheses on this point in the discussion and add a summary figure to highlight the specific role of malectin.

Given the likelihood that malectin plays a role in the glycosylation of heavily glycosylated proteins like Spike, it is unfortunate that only 5 glycosites on Spike were identified using the MS deamidation assay when Spike has a large number of glycans (~22 sites). The mass spec data set would also include endogenous proteins. Were any heavily glycosylated endogenous proteins hypoglycosylated in the MS analysis in Fig 5D?

We plan to interrogate this question in our existing MS deamidation proteomics data set as outlined above.

The inclusion of the nsp4 interactome and its partial characterization is a distraction from the storyline that focuses on malectin and nsp2.

We believe the nsp4 comparative interactome and functional genomics data offers a rich resource for further functional investigation by others, if made public. While we found the malectin and nsp2 storyline the most compelling to pursue, we believe the inclusion of the nsp4 data strengthens the overall approach, in agreement with Reviewer #3’s comments.

Reviewer #3 (Public Review):

Summary:

In this study, Davies and Plate set out to discover conserved host interactors of coronavirus non-structural proteins (Nsp). They used 293T cells to ectopically express flag-tagged Nsp2 and Nsp4 from five human and mouse coronaviruses, including SARS-CoV-1 and 2, and analyzed their interaction with host proteins by affinity purification mass-spectrometry (AP-MS). To confirm whether such interactors play a role in coronavirus infection, the authors measured the effects of individual knockdowns on replication of murine hepatitis virus (MHV) in mouse Delayed Brain Tumor cells. Using this approach, they identified a previously undescribed interactor of Nsp2, Malectin (Mlec), which is involved in glycoprotein processing and shows a potent pro-viral function in both MHV and SARS-CoV-2. Although the authors were unable to confirm this interaction in MHV-infected cells, they show that infection remodels many other Mlec interactions, recruiting it to the ER complex that catalyzes protein glycosylation (OST). Mlec knockdown reduced viral RNA and protein levels during MHV infection, although such effects were not limited to specific viral proteins. However, knockdown reduced the levels of five viral glycopeptides that map to Spike protein, suggesting it may be affected by Mlec.

Strengths:

This is an elegant study that uses a state-of-the-art quantitative proteomic approach to identify host proteins that play critical roles in viral infection. Instead of focusing on a single protein from a single virus, it compares the interactomes of two viral proteins from five related viruses, generating a high confidence dataset. The functional follow-ups using multiple live and reporter viruses, including MHV and CoV2 variants, convincingly depict a pro-viral role for Mlec, a protein not previously implicated in coronavirus biology.

Weaknesses:

Although a commonly used approach, AP-MS of ectopically expressed viral proteins may not accurately capture infection-related interactions. The authors observed Mlec-Nsp2 interactions in transfected 293T cells (1C) but were unable to reproduce those in mouse cells infected with MHV (3C). EIF4E2/GIGYF2, two bonafide interactors of CoV2 Nsp2 from previous studies, are listed as depleted compared to negative controls (S1D). Most other CoV2 Nsp2 interactors are also depleted by the same analysis (S1D). Previously reported MERS Nsp2 interactors, including ASCC1 and TCF25, are also not detected (S1D). Furthermore, although GIGYF2 was not identified as an interactor of MHV Nsp2/4 in human cells (S1D), its knockdown in mouse cells reduced MHV titers about 1000 fold (S4). The authors should attempt to explain these discrepancies.

We plan to address these discrepancies with further elaboration in the text.

More importantly, the authors were unable to establish a direct link between Mlec and the biogenesis of any viral or host proteins, by mass-spectrometry or otherwise. Although it is clear that Mlec promotes coronavirus infection, the mechanism remains unclear. Its knockdown does not affect the proteome composition of uninfected cells (S15B), suggesting it is not required for proteome maintenance under normal conditions. The only viral glycopeptides detected during MHV infection originated from Spike (5D), although other viral proteins are also known to be glycosylated. Cells depleted for Mlec produce ~4-fold less Spike protein (4E) but no more than 2-fold less glycosylated spike peptides (5D), compounding the interpretation of Mlec effects on viral protein biogenesis. Furthermore, Spike is not essential for the pro-viral role of Mlec, given that Mlec knockdown reduces replication of SARS-CoV-2 replicons that express all viral proteins except for Spike (6A/B).

These are all important points. We plan to acknowledge some of these compounding factors in the Discussion.

Any of the observed effects on viral protein levels could be secondary to multiple other processes. Interventions that delay infection for any reason could lead to an imbalance of viral protein levels because Spike and other structural proteins are produced at a much higher rate than non-structural proteins due to the higher abundance of their cognate subgenomic RNAs. Similarly, the observation that Mlec depletion attenuates MHV-mediated changes to the host proteome (S15C/D) can also be attributed to indirect effects on viral replication, regardless of glycoprotein processing. In the discussion, the authors acknowledge that Mlec may indirectly affect infection through modulation of replication complex formation or ER stress, but do not offer any supporting evidence. Interestingly, plant homologs of Mlec are implicated in innate immunity, favoring a more global role for Mlec in mammalian coronavirus infections.

We plan to interrogate our existing proteomics data for signatures of ER stress in Mlec-depleted cells (as outlined above).

Finally, the observation that both Nsp2 (3C) and Mlec (3E/F) are recruited to the OST complex during MHV infection neither support nor refute any of these alternate hypotheses, given that Mlec is known to interact with OST in uninfected cells and that Nsp2 may interact with OST as part of the full length unprocessed Orf1a, as it co-translationally translocates into the ER. Therefore, the main claims about the role of Mlec in coronavirus protein biogenesis are only partially supported.

We plan to acknowledge this alternative hypothesis in the Discussion.

eLife assessment

This important study provides substantial technical development for neural circuit tracing in larval zebrafish, a widely used model for systems and developmental neurobiology, and the tool could greatly benefit neural circuit research by enabling a detailed investigation of circuit structure and function in a major model organism. The supporting evidence is solid, although a more detailed description of validation experiments would have increased confidence in the technique's utility. The work will interest zebrafish neurobiologists who are working on identifying novel neuronal connectivity patterns, provided that reagents generated in this study are made widely available; issues such as glial cell labeling, detailed toxicity analysis, and the impact of virus dose on tracing efficiency need further exploration to enhance the findings' applicability and robustness.

Reviewer #1 (Public Review):

EnvA-pseudotyped glycoprotein-deleted rabies virus has emerged as an essential tool for tracing monosynaptic inputs to genetically defined neuron populations in the mammalian brain. Recently, in addition to the SAD B19 rabies virus strain first described by Callaway and colleagues in 2007, the CVS N2c rabies virus strain has become popular due to its low toxicity and high trans-synaptic transfer efficiency. However, despite its widespread use in the mammalian brain, particularly in mice, the application of this cell-type-specific monosynaptic rabies tracing system in zebrafish has been limited by low labeling efficiency and high toxicity. In this manuscript, the authors aimed to develop an efficient retrograde monosynaptic rabies-mediated circuit mapping tool for larval zebrafish. Given the translucent nature of larval zebrafish, whole-brain neuronal activities can be monitored, perturbed, and recorded over time. Introducing a robust circuit mapping tool for larval zebrafish would enable researchers to simultaneously investigate the structure and function of neural circuits, which would be of significant interest to the neural circuit research community. Furthermore, the ability to track rabies-labeled cells over time in the transparent brain could enhance our understanding of the trans-synaptic retrograde tracing mechanism of the rabies virus.

To establish an efficient rabies virus tracing system in the larval zebrafish brain, the authors conducted meticulous side-by-side experiments to determine the optimal combination of trans-expressed rabies G proteins, TVA receptors, and recombinant rabies virus strains. Consistent with observations in the mouse brain, the CVS N2c strain trans-complemented with N2cG was found to be superior to the SAD B19 combination, offering lower toxicity and higher efficiency in labeling presynaptic neurons. Additionally, the authors tested various temperatures for the larvae post-virus injection and identified 36{degree sign}C as the optimal temperature for improved virus labeling. They then validated the system in the cerebellar circuits, noting evolutionary conservation in the cerebellar structure between zebrafish and mammals. The monosynaptic inputs to Purkinje cells from granule cells were neatly confirmed through ablation experiments.

However, there are a couple of issues that this study should address. Additionally, conducting some extra experiments could provide valuable information to the broader research field utilizing recombinant rabies viruses as retrograde tracers.

(1) It was observed that many radial glia were labeled, which casts doubt on the specificity of trans-synaptic spread between neurons. The issues of transneuronal labeling of glial cells should be addressed and discussed in more detail. In this manuscript, the authors used a transgenic zebrafish line carrying a neuron-specific Cre-dependent reporter and EnvA-CVS N2c(dG)-Cre virus to avoid the visualization of virally infected glial cells. However, this does not solve the real issue of glial cell labeling and the possibility of a non-synaptic spread mechanism.

In addition, wrong citations in Line 307 were made when referring to previous studies discovering the same issue of RVdG-based transneuronal labeling radial glial cells.

"The RVdG-based transneuronal labeling of radial glial cells was commonly observed in larval zebrafish29,30".

The cited work was conducted using vesicular stomatitis virus (VSV). A more thorough analysis and/or discussion on this topic should be included. Several key questions should be addressed:

Does the number of labeled glial cells increase over time?<br /> Do they increase at the same rate over time as labeled neurons?<br /> Are the labeled glial cells only present around the injection site?<br /> Can the phenomenon of transneuronal labeling of radial glial cells be mitigated if the tracing is done in slightly older larvae?<br /> What is the survival rate of the infected glial cells over time?<br /> If an infected glial cell dies due to infection or gets ablated, does the rabies virus spread from the dead glial cells?<br /> If TVA and rabies G are delivered to glial cells, followed by rabies virus injection, will it lead to the infection of other glial cells or neurons?

Answers to any of these questions could greatly benefit the broader research community.

(2) The optimal virus tracing effect has to be achieved by raising the injected larvae at 36C. Since the routine temperature of zebrafish culture is around 28C, a more thorough characterization of the effect on the health of zebrafish should be conducted.

(3) Given the ability of time-lapse imaging of the infected larval zebrafish brain, the system can be taken advantage of to tackle important issues of rabies virus tracing tools.<br /> a) Toxicity.<br /> The toxicity of rabies viruses is an important issue that limits their application and affects the interpretation of traced circuits. For example, if a significant proportion of starter cells die before analysis, the traced presynaptic networks cannot be reliably assigned to a "defined" population of starter cells. In this manuscript, the authors did an excellent job of characterizing the effects of different rabies strains, G proteins derived from various strains, and levels of G protein expression on starter cell survival. However, an additional parameter that should be tested is the dose of rabies virus injection. The current method section states that all rabies virus preparations were diluted to 2x10^8 infection units per ml, and 2-5 nl of virus suspension was injected near the target cells. It would be interesting to know the impact of the dose/volume of virus injection on retrograde tracing efficiency and toxicity. Would higher titers of the virus lead to more efficient labeling but stronger toxicities? What would be the optimal dose/volume to balance efficiency and toxicity? Addressing these questions would provide valuable insights and help optimize the use of rabies viruses for circuit tracing.

b) Primary starters and secondary starters:<br /> Given that the trans-expression of TVA and G is widespread, there is the possibility of coexistence of starter cells from the initial infection (primary starters) and starter cells generated by rabies virus spreading from the primary starters to presynaptic neurons expressing G. This means that the labeled input cells could be a mixed population connected with either the primary or secondary starter cells.

It would be immensely interesting if time-lapse imaging could be utilized to observe the appearance of such primary and secondary starter cells. Assuming there is a time difference between the initial appearance of these two populations, it may be possible to differentiate the input cells wired to these populations based on a similar temporal difference in their initial appearance. This approach could provide valuable insights into the dynamics of rabies virus spread and the connectivity of neural circuits.

Reviewer #2 (Public Review):

The study by Chen, Deng et al. aims to develop an efficient viral transneuronal tracing method that allows efficient retrograde tracing in the larval zebrafish. The authors utilize pseudotyped-rabies virus that can be targeted to specific cell types using the EnvA-TvA systems. Pseudotyped rabies virus has been used extensively in rodent models and, in recent years, has begun to be developed for use in adult zebrafish. However, compared to rodents, the efficiency of the spread in adult zebrafish is very low (~one upstream neuron labeled per starter cell). Additionally, there is limited evidence of retrograde tracing with pseudotyped rabies in the larval stage, which is the stage when most functional neural imaging studies are done in the field. In this study, the authors systematically optimized several parameters of rabies tracing, including different rabies virus strains, glycoprotein types, temperatures, expression construct designs, and elimination of glial labeling. The optimal configurations developed by the authors are up to 5-10 fold higher than more typically used configurations.

The results are solid and support the conclusions. However, the methods should be described in more detail to allow other zebrafish researchers to apply this method in their own work.

Additionally, some findings are presented anecdotally, i.e., without quantification or sufficient detail to allow close examinations. Lastly, there is concern that the reagents created by the authors will not be easily accessible to the zebrafish community.

(1) The titer used in each experiment was not stated. In the methods section, it is stated that aliquots are stored at 2x10e8. Is it diluted for injection? Are all of the experiments in the manuscripts with the same titer?

2) The age for injection is quite broad (3-5 dpf in Fig 1 and 4-6 dpf in Fig 2). Given that viral spread efficiency is usually more robust in younger animals, describing the exact injection age for each experiment is critical.

(3) More details should be provided for the paired electrical stimulation-calcium imaging study. How many GC cells were tested? How many had corresponding PC cell responses? What is the response latency? For example, images of stimulated and recorded GCs and PCs should be shown.

(4) It is unclear how connectivity between specific PC and GC is determined for single neuron connectivity. In other images (Figure 4C), there are usually multiple starter cells and many GCs. It was not shown that the image resolution can establish clear axon-dendritic contacts between cell pairs.

Reviewer #3 (Public Review):

Summary:

The authors establish reagents and define experimental parameters useful for defining neurons retrograde to a neuron of interest.

Strengths:

A clever approach, careful optimization, novel reagents, and convincing data together lead to convincing conclusions.

Weaknesses:

In the current version of the manuscript, the tracing results could be better centered with respect to past work, certain methods could be presented more clearly, and other approaches worth considering.

Appraisal/Discussion:

Trans-neuronal tracing in the larval zebrafish preparation has lagged behind rodent models, limiting "circuit-cracking" experiments. Previous work has demonstrated that pseudotyped rabies virus-mediated tracing could work, but published data suggested that there was considerable room for optimization. The authors take a major step forward here, identifying a number of key parameters to achieve success and establishing new transgenic reagents that incorporate modern intersectional approaches. As a proof of concept, the manuscript concludes with a rough characterization of inputs to cerebellar Purkinje cells. The work will be of considerable interest to neuroscientists who use the zebrafish model.

Author response:

We are grateful to the reviewers for their insightful comments on our manuscript and are encouraged by their overall favorable assessments. For the eLife Version of Record, we will make the following revisions to address reviewers’ comments and broaden the applicability of our technique in the zebrafish research community:

(1) We will elaborate on various facets with additional details:

a) Experimental conditions | We will specify the transgenic background, injected plasmids, larval stage, viral type, and viral titer clearly for each related experiment.

b) Experimental methods | We will depict in more details on how to inject the virus into a target area in larval zebrafish.

c) Data analysis | We will provide more detailed information on the paired electrical stimulation-calcium imaging study and on identifying connected Purkinje cells and granule cells during circuit reconstruction.

d) Discussion | We will elaborate on trans-synaptic specificity concerning glial cell labeling, toxicity related to viral dose and temperature, and the potential issue of secondary starters and multi-step circuit tracing.

(2) We will address the issue of glial cell labeling by adding more discussion and characterization, including potential mechanisms and implications, cell distribution, labeling progress, survival, and capability for viral transmission as starter cells.

(3) We will modify the text of the manuscript to clarify additional points raised by the reviewers.

(4) We will provide public repositories for accessing both the items and information on zebrafish lines, plasmids, viral vectors, and reconstructed data generated in this study.

In the end, we will submit full responses to the reviewer comments along with the revised version of the manuscript.

eLife assessment

The manuscript establishes a sophisticated mouse model for acute retinal artery occlusion (RAO) by combining unilateral pterygopalatine ophthalmic artery occlusion (UPOAO) with a silicone wire embolus and carotid artery ligation, generating ischemia-reperfusion injury upon removal of the embolus. This clinically relevant model is useful for studying the cellular and molecular mechanisms of RAO. The data overall are solid, presenting a novel tool for screening pathogenic genes and promoting further therapeutic research in RAO.

Reviewer #1 (Public Review):

Summary:

Wang, Y. et al. used a silicone wire embolus to definitively and acutely clot the pterygopalatine ophthalmic artery in addition to carotid artery ligation to completely block blood supply to the mouse inner retina, which mimic clinical acute retinal artery occlusion. A detailed characterization of this mouse model determined the time course of inner retina degeneration and associated functional deficits, which closely mimic human patients. Whole retina transcriptome profiling and comparison revealed distinct features associated with ischemia, reperfusion, and different model mechanisms. Interestingly and importantly, this team found a sequential event including reperfusion-induced leukocyte infiltration from blood vessels, residual microglial activation, and neuroinflammation that may lead to neuronal cell death.

Strengths:

Clear demonstration of the surgery procedure with informative illustrations, images, and superb surgical videos.<br /> Two time points of ischemia and reperfusion were studied with convincing histological and in vivo data to demonstrate the time course of various changes in retinal neuronal cell survivals, ERG functions, and inner/outer retina thickness.<br /> The transcriptome comparison among different retinal artery occlusion models provides informative evidence to differentiate these models.<br /> The potential applications of the in vivo retinal ischemia-reperfusion model and relevant readouts demonstrated by this study will certainly inspire further investigation of the dynamic morphological and functional changes of retinal neurons and glial cell responses during disease progression and before and after treatments.

Weaknesses:

It would be beneficial to the manuscript and the readers if the authors could improve the English of this manuscript by correcting obvious grammar errors, eliminating many of the acronyms that are not commonly used by the field, and providing a reason why this complicated but clever surgery procedure was designed and a summary table with time course of all the morphological, functional, cellular, and transcriptome changes associated with this model.

Reviewer #2 (Public Review):

Summary:

The authors of this manuscript aim to develop a novel animal model to accurately simulate the retinal ischemic process in retinal artery occlusion (RAO). A unilateral pterygopalatine ophthalmic artery occlusion (UPOAO) mouse model was established using silicone wire embolization combined with carotid artery ligation. This manuscript provided data to show the changes of major classes of retinal neural cells and visual dysfunction following various durations of ischemia (30 minutes and 60 minutes) and reperfusion (3 days and 7 days) after UPOAO. Additionally, transcriptomics was utilized to investigate the transcriptional changes and elucidate changes in the pathophysiological process in the UPOAO model post-ischemia and reperfusion. Furthermore, the authors compared transcriptomic differences between the UPOAO model and other retinal ischemic-reperfusion models, including HIOP and UCCAO, and revealed unique pathological processes.

Strengths:

The UPOAO model represents a novel approach for studying retinal artery occlusion. The study is very comprehensive.

Weaknesses:

Originally, some statements were incorrect and confusing. However, the authors have made clarifications in the revised manuscript to avoid confusion.

Author response:

The following is the authors’ response to the original reviews.

eLife assessment:

The manuscript establishes a sophisticated mouse model for acute retinal artery occlusion (RAO) by combining unilateral pterygopalatine ophthalmic artery occlusion (UPOAO) with a silicone wire embolus and carotid artery ligation, generating ischemia-reperfusion injury upon removal of the embolus. This clinically relevant model is useful for studying the cellular and molecular mechanisms of RAO. The data overall are solid, presenting a novel tool for screening pathogenic genes and promoting further therapeutic research in RAO.

Thank you for recognizing the sophistication and clinical relevance of our mouse model for acute retinal artery occlusion. We are grateful for your supportive feedback.

Public reviews:

(1) Response to Reviewer #1: 

Summary:

Wang, Y. et al. used a silicone wire embolus to definitively and acutely clot the pterygopalatine ophthalmic artery in addition to carotid artery ligation to completely block the blood supply to the mouse inner retina, which mimics clinical acute retinal artery occlusion. A detailed characterization of this mouse model determined the time course of inner retina degeneration and associated functional deficits, which closely mimic human patients. Whole retina transcriptome profiling and comparison revealed distinct features associated with ischemia, reperfusion, and different model mechanisms. Interestingly and importantly, this team found a sequential event including reperfusion-induced leukocyte infiltration from blood vessels, residual microglial activation, and neuroinflammation that may lead to neuronal cell death.

Strengths:

Clear demonstration of the surgery procedure with informative illustrations, images, and superb surgical videos.

Two-time points of ischemia and reperfusion were studied with convincing histological and in vivo data to demonstrate the time course of various changes in retinal neuronal cell survivals, ERG functions, and inner/outer retina thickness.

The transcriptome comparison among different retinal artery occlusion models provides informative evidence to differentiate these models.

The potential applications of the in vivo retinal ischemia-reperfusion model and relevant readouts demonstrated by this study will certainly inspire further investigation of the dynamic morphological and functional changes of retinal neurons and glial cell responses during disease progression and before and after treatments.

We sincerely appreciate your detailed and positive feedback. These evaluations are invaluable in highlighting the significance and impact of our work. Thank you for your thoughtful and supportive review.

Weaknesses:

It would be beneficial to the manuscript and the readers if the authors could improve the English of this manuscript by correcting obvious grammar errors, eliminating many of the acronyms that are not commonly used by the field, and providing a reason why this complicated but clever surgery procedure was designed and a summary table with the time course of all the morphological, functional, cellular, and transcriptome changes associated with this model.

Thank you for your thorough review of the manuscript. We sincerely apologize for any grammatical errors resulting from our English language proficiency and have taken the necessary steps to polish the article. Additionally, we have heeded your advice and reduced the use of field-specific acronyms to enhance readability for both the manuscript and its readers.

Regarding the rationale behind the design of the UPOAO model, we have provided a description in Introduction section. Our group focuses on the research of pathogenesis and clinical treatment for RAO. The absence of an accurate mouse model simulating the retinal ischemic process has hampered progress in developing neuroprotective agents for RAO. To better simulate the retinal ischemic process and possible ischemia-reperfusion injury following RAO, we developed a novel vascular-associated mouse model called the unilateral pterygopalatine ophthalmic artery occlusion (UPOAO) model. We drew inspiration from the widely employed middle cerebral artery occlusion (MCAO) model, commonly used in cerebral ischemic injury research, which guided the development of the UPOAO model.

We appreciate your valuable suggestion regarding the inclusion of a summary table outlining the time course of morphological, functional, cellular, and transcriptome changes associated with this model. To address this, we intend to include a supplementary table at the end of the article (Table. S2 Summary Table), which will offer a comprehensive overview of the experimental results, thereby aiding in clarity and interpretation.

Once again, we thank you for your insightful comments and suggestions, which have greatly contributed to the improvement of our manuscript.

(2) Response to Reviewer #2: 

Summary:

The authors of this manuscript aim to develop a novel animal model to accurately simulate the retinal ischemic process in retinal artery occlusion (RAO). A unilateral pterygopalatine ophthalmic artery occlusion (UPOAO) mouse model was established using silicone wire embolization combined with carotid artery ligation. This manuscript provided data to show the changes in major classes of retinal neural cells and visual dysfunction following various durations of ischemia (30 minutes and 60 minutes) and reperfusion (3 days and 7 days) after UPOAO. Additionally, transcriptomics was utilized to investigate the transcriptional changes and elucidate changes in the pathophysiological process in the UPOAO model post-ischemia and reperfusion. Furthermore, the authors compared transcriptomic differences between the UPOAO model and other retinal ischemic-reperfusion models, including HIOP and UCCAO, and revealed unique pathological processes.

Strengths:

The UPOAO model represents a novel approach to studying retinal artery occlusion. The study is very comprehensive.

We greatly appreciate your positive assessment of our work and are encouraged by your recognition of its significance.

Weaknesses:

Some statements are incorrect and confusing. It would be helpful to review and clarify these to ensure accuracy and improve readability.

We sincerely appreciate your meticulous review of the manuscript. Taking into account your valuable feedback, we will thoroughly address the inaccuracies identified in the revised version. Additionally, we will commit to polishing the article to ensure improved readability. We apologize for any confusion caused by these inaccuracies and genuinely thank you for bringing them to our attention.

Recommendations For The Authors:

Reviewer #1:

(1) Response to comment:

The conclusions of this paper are mostly well supported by clear images and convincing data analysis, but some aspects of image presentation and additional data analysis may be needed to strengthen the manuscript.

We sincerely appreciate your positive assessment of our work and your recognition of the clear images and convincing data analysis supporting our conclusions. Your constructive feedback on enhancing the clarity of our manuscript's image presentation and additional data analysis is highly valued. In response to your suggestions, we have taken steps to improve readability by removing or correcting uncommon acronyms from certain images. We have also conducted further data analysis to provide more comprehensive insights. Thank you for your guidance in improving the quality of our manuscript.

(2) Response to recommendation (1):

In Results 3.1 or in Method 2.2: please explain why this combination of silicone wire embolization and carotid artery ligation was chosen to replace previous models such as UCCAO? What are the advantages? And why the silicone wire embolus was inserted through ECA instead of inserting into CCA directly? The cleverly designed surgical procedure is very impressive but the reasoning behind it is not obvious and needs more explanation.

Thank you for your valuable feedback.

In the introduction, we briefly describe the rationale for developing the UPOAO model to simulate acute ischemia-reperfusion of retinal artery occlusion (RAO). Previous common retinal ischemia model had certain shortcomings. For example, in the HIOP model, which is often used for simulating glaucoma, the ischemic factor of interrupted retinal blood flow may be amplified due to the dual effects of IOP-induced mechanical stress [1, 2] and vascular ischemia due to normal saline perfusion in the anterior chamber. In the UCCAO model, recanalization is performed after ligation of the carotid blood vessels, and the retina communicates with the blood vessels in the brain, resulting in retinal hypoperfusion. The retina ischemia in UCCAO is a chronical process, for example, the retina became thinner at week 10 and week 15 [3], while RAO is an acute total retinal ischemic disease. Therefore, it is critically important to develop a simple mouse model that can simulate acute retinal ischemia and reperfusion injury in RAO patients.

Various models have been developed for ischemic stroke research, with the endoluminal suture model being the most employed method for middle cerebral artery occlusion (MCAO). In this model, filaments are introduced through either the external or internal carotid artery and advanced into the middle cerebral artery, causing temporary blood flow blockage for a specific duration. This method has been extensively employed in studies involving transient occlusion [4]. Among the MCAO models, the Koizumi method (occlusion from the common carotid artery (CCA) to the middle cerebral artery (MCA)) and the Longa method (occlusion from the external carotid artery (ECA) to the MCA) are frequently used. Among these two methods, the Longa method is more widely utilized in research studies. The Longa method has a much lower mortality rate post-surgery (26%) than that of the Koizumi (44%) [5]. The MCAO model induces substantial infarct areas and significantly contributes to advancements in stroke research, including investigations into blood-brain barrier disruption and inflammatory responses to ischemia.

RAO is considered a form of ocular stroke. Inspired by the MCAO model, we have employed a silicone wire embolus to induce acute interruption of blood flow to the retina. This approach enables the investigation of pathophysiological processes associated with RAO, providing valuable insights into the understanding of this condition. We have clarified these points in the revised manuscript (line 129).

The reasoning behind inserting the silicone wire embolus through the ECA instead of directly into the CCA is twofold:

(1) Convenience and avoidance of heavy bleeding and mortality. Inserting the silicone wire embolus requires creating an opening in the artery, which then needs to be ligated at both ends after the silicone wire embolus is removed to prevent excessive bleeding. The ECA's ability to form a straight line with the ICA after folding makes it more convenient for the entry and removal of the silicone wire embolus. This procedure is more convenient to perform on the ECA. The blood flow to the CCA can be restored after the plug is removed from ECA, ensuring that the blood supply to the brain through the CCA is not affected.

(2) Preservation of reperfusion process. If the silicone wire embolus were inserted directly into the CCA, the ends of the CCA opening would need to be ligated after the silicone wire embolus is removed. This would result in a lack of reperfusion process after retinal ischemia. To enable the reperfusion process, the decision was made to open the ECA instead.

We have clarified these points in the revised manuscript to better explain the rationale behind our methodology (line 139). Thank you for prompting this important clarification, which we believe will enhance the understanding of our readers.

(3) Response to recommendation (2):

Did the UPOPA actually block OA, including both the retinal (CRA) and choroidal (SPCA and LPCA) blood supply? If so, why does it seem only the inner retina was affected but not the outer retina?

Thank you for your question. We agree with you that the UPOAO model blocks OA, which includes retinal and choroidal vessels. Our experimental results primarily indicate damage to the inner retinal layer within 7 days of reperfusion. For example, OCT and HE staining showed significant thinning of the inner retina after 60 minutes of ischemia followed by 7 days of reperfusion (Figure 4). At the same time, the b-wave amplitudes were decreases, usually indicating damage to the inner layer of the retina. However, the outer retina was seemed not affected by 60 minutes of ischemia based on the results of OCT, HE and immunofluorescence.

Inner layer of the retina was known to show the highest sensitivity to hypoxic challenges [6], whereas the outer retinal layer was more resistant to hypoxic stress [7]. The possible reason for these results was that the outer layer like photoreceptors is more tolerant against ischemia than inner layer of the retina. Previous studies of retinal ischemia-reperfusion models supported this assumption. In the UCCAO model, the b-wave was more affected than the a-wave. Decreases in the amplitudes of OPs, scotopic b-wave, and photopic b-wave were consistently observed on week 4 after UCCAO, while the amplitude of scotopic a-wave did not dramatically change [8]. Prolonged ischemia, such as permanent ischemia, led to photoreceptor cell degradation, as seen in Stevens et al.'s report of photoreceptors loss 3 months after permanent ligation of both common carotid arteries in bilateral common carotid artery occlusion (BCCAO) [9]. In the HIOP model, the GCL and INL reacted sensitively to ischemic processes. A significant thinning of the GCL as early as 6 hours after 60 minutes of ischemia [10]. Horizontal cells and photoreceptors remained mostly unaffected, while most RGCs and several amacrine cell subtypes disappear [11, 12].

Our study revealed the changes that occurred within 60 minutes of ischemia and the first 7 days of reperfusion in the UPOAO model. One possibility was that the ischemia duration in our model was not long enough to affect the outer retinal cells. Furthermore, the observation time point for reperfusion was not long enough to see the structure damage and visual dysfunctions in the outer retinal layer. As we have explained in the manuscript, further exploration is needed to understand changes induced by longer ischemia duration and reperfusion periods. Revealing the damage to retinal structure and function during longer ischemia time will be an emphasis direction for our further research.

(4) Response to recommendation (3):

Better to only use well-accepted acronyms and remove those that are rarely seen in other publications, such as IMRL, MRL, HIOP, TRT, etc.

Thank you for your valuable feedback. In our manuscript, we utilized the Spectralis HRA+OCT device (Heidelberg) to capture the retinal images. However, the resulting image layering did not adequately distinguish each retinal layer clearly. To address this limitation, we referred to a clinical OCT stratification approach in RVO and divided the retina into the inner, middle, and outer layers [16]. We acknowledge that this hierarchical description is not commonly used and have therefore followed your recommendation to remove these rare acronyms and instead employ the layer structure abbreviation along with the plus sign. The methods and results have been revised accordingly (line 213, line 368, Figure 4 and Figure S2).

In addition, for the HIOP model, it is also known as the IR or RIRI model [17-19], and the pathophysiological process of retinal ischemia-reperfusion injury (IRI) is usually used to represent this type of anterior chamber perfusion model. To avoid confusion between the pathophysiological process of ischemia-reperfusion studied in this paper and the common model of high intraocular pressure, we have consistently referred to it as the HIOP model, an abbreviation that is cited in many references [20-22].

Thanks again for the suggestion. We apologize for any confusion caused by the use of abbreviations and have made the necessary corrections in the manuscript. We have also strengthened the details of OCT layering in the images to enhance readability for our audience.

(5) Response to recommendation (4):

Figure 3F, G: What do the OP changes mean? What retina cell dysfunction leads to OP changes? Is there RGC-relevant visual function readout to correlate with RGC death?

Oscillatory potentials (OPs) are important components of the electroretinogram (ERG). While the precise origin of OPs remains unclear, they are generally believed to be generated from the inner retinal layer, specifically involving bipolar cells, amacrine cells and ganglion cells [23]. OPs are sensitive indicators of retinal ischemic effects and can detect dysfunction before alterations in the b-waves occur [24-26] (We have added these statements at line 358). In this research, the reduction of OPs indicated dysfunction in the inner retinal layer and retinal ischemia.

The function of RGCs can be non-invasively assessed by using various ERG technique that emphasize the activity of inner retina neurons, including OPs of multifocal ERG (mfERG), photopic negative response (PhNR) in mfERG, pattern electroretinogram (PERG), negative Scotopic Threshold Response (nSTR) [27]. Among these indicators, the PERG appears to be more specifically related to the presence of functional RGCs. However, the complexity of electrophysiological sources and species-specific differences in RGCs characteristics should also be considered. In addition, visual evoked potentials (VEP) can assess the function of visual signaling in the whole visual pathway from RGC axons to the visual cortex of the brain [28, 29]. Unfortunately, due to the unavailability of specific equipment required for evaluating RGCs function, we encountered limitations in conducting a comprehensive assessment in this study. This limitation emphasizes the importance of future studies incorporating RGCs evaluation to provide a more comprehensive understanding of visual pathway functionality and its implications, considering indicators such as PERG and PhNR.

Thank you for your careful review and insightful questions.

(6) Response to recommendation (5):

Figure 4B: RNFL/GCL/IPL normally called GCC (ganglion cell complex).

We appreciate your helpful recommendation regarding the abbreviation GCC (ganglion cell complex) for the combination of RNFL, GCL, and IPL. We have updated this terminology in the revised manuscript (line 213 and Figure 4).

(7) Response to recommendation (6):

Figure 4 A-F: Normally a circular OCT image surrounding the optic nerve head is preferred to measure retina thickness. If in these figures, all the OCT images are from the same location, it may be acceptable, but need to provide imaging details on how these OCT planes are selected and what has been done to make sure the same locations were selected for comparison.

We agree with your comment on OCT imaging that the retina is usually captured OCT images surrounding the optic nerve head. In this study, our goal was to assess both the thickness of the peripheral retina and the retina near the optic nerve head. To achieve this, we considered the optic nerve head as the apex of the selected field of view (left upper region of panel A in Figure 4). For each mouse, we obtained OCT images of the superior nasal (SN), superior temporal (ST), inferior nasal (IN), and inferior temporal (IT) fields of the optic nerve. We then averaged the thicknesses from these four fields. In each field, we measured and statistically evaluated the retinal thickness at distances of 1.5, 3, and 4.5 papillae diameters (PD) from the optic nerve head.

This approach allowed us to ensure that the same locations were selected for comparison and provided a comprehensive assessment of retinal thickness across different regions. We have detailed this methodology in the revised manuscript to clarify the imaging process and the consistency of the selected locations.

Thank you for your insightful feedback.

Reviewer #2:

Addressing the following concerns is necessary to improve the manuscript.

(1) Response to recommendation (1):

The manuscript contains many grammatical errors and should be carefully reviewed for corrections. For example: In the title, "Silicone Wire Embolization-induced Acute Retinal Artery Ischemia and Reperfusion Model in Mouse: Gene Expression Provide Insight into Pathological Processes". It should be "Provides" instead of "Provide". In the Abstract, "The resident microglia within the retina and peripheral leukocytes which access to the retina were pronounced increased on reperfusion periods." It should be "pronouncedly" or "markedly" instead of " pronounced".

Thank you for your careful reading and pointing out the grammatical errors in the manuscript. We apologize for these mistakes and have since revised and polished the article with the assistance of native English speakers. Ensuring accurate and clear language usage in scientific writing is crucial, and we appreciate your help in improving the quality of our manuscript. Thank you for bringing these errors to our attention.

(2) Response to recommendation (2):

Video 2: the video content from "30s-47s" and "50s-67s" is repeatedly shown.

Thank you for your careful review of the video. In the process of preparing the external carotid artery for silicone wire embolus insertion, we first ligated the distal end with a square knot and then tied a loose knot at the proximal end. In the video content from "30s-47s" and "50s-67s", we are tying a square knot. We apologize for any confusion caused by these repeated video clips.

(3) Response to recommendation (3):

Figure 1: The ConA staining (H-I) and FFA (J-K) were performed before the removal of silicone wire embolus. It would be beneficial to clarify this in the figure legend too. Additionally, the label 'Post. Sup. Alveolar art.: Posterior superior alveolar artery' is not present in Figure 1L."

Thank you for your thorough review of the manuscript and the valuable suggestions regarding Figure 1. We have updated the figure legend of Figure 1 to clarify that ConA staining (H-I) and FFA (J-K) were performed before the removal of the silicone wire embolus (line 868 and line 873). Additionally, we have included the label 'Post. Sup. Alveolar art' in Figure 1L as you pointed out. We appreciate your careful attention to detail, and we have ensured that these omissions have been rectified in the revised version of the manuscript.

(4) Response to recommendation (4):

Figure 2: only representative images of RGCs at the peripheral retina were shown. It is not clear if only RGCs in the peripheral retina were quantified. Is there RGC loss in the central and middle retina in the UPOAO model as well? How many fields of RGCs were quantified for each retina?

Thank you for your meticulous review of the manuscript. The quantification method of RGCs is described in detail as follows:

Four radial incisions were made in the retina and flattened on a glass slide to create a "four-leaf clover" shape. Retina was photographed using a fluorescence microscope (BX63, Olympus, Japan). We captured images from three different regions of each retinal quadrant: 0.1 mm-0.5 mm (central region, field numbers: 1, 4, 7, 10), 0.9 mm-1.3 mm (middle region, field numbers: 2, 5, 8, 11), and 1.7 mm-2.1 mm (peripheral region, field numbers: 3, 6, 9, 12) from the optic nerve head, respectively, as shown in Author response image 1.

Of these, the peripheral field changes were the most noticeable, so we used the Leica SP8 confocal microscope (20X) to capture peripheral field RGCs as a demonstration (Figure 2A, C, E, G). RGC counts of twelve fields of each retina were quantified and the average density of RGCs in twelve fields per retina was shown in Figure 2B, D, F, K. RGC counts in the central (field number: 1, 4, 7, 10), middle (field number: 2, 5, 8, 11), and peripheral (field number: 3, 6, 9, 12) visual fields were shown in Author response table 1-4.We have included this detailed methodology in the revised manuscript to clarify the quantification process and to address the presence of RGCs loss in both the central and middle retina in the UPOAO model. Thank you for pointing out the need for this clarification.

Author response image 1.

Schematic diagram of field selection. Scale bar=1.4 mm. Each retinal petal has three distinct visual fields (the area circled by the green line) that radiate from the optic nerve head to the periphery, in that order, the central, middle, and peripheral visual fields.

Author response table 1.

RGCs counts in each field of each retina (30-minute ischemia and 3-day reperfusion)

Author response table 2.

RGCs counts in each field of each retina (30-minute ischemia and 7-day reperfusion)

Author response table 3.

RGCs counts in each field of each retina (60-minute ischemia and 3-day reperfusion)

Author response table 4.

RGCs counts in each field of each retina (60-minute ischemia and 7-day reperfusion)

(5) Response to recommendation (5):

Figure 3: The representative wave lines in panels A (60min_3d, 60min_7d) and F do not reflect the statistical analysis presented in panels D, E, and G, especially for the amplitudes of b waves and OPs.

Thank you for your careful review of the manuscript. We've added labels for a-waves, b-waves, and improved the presentation of OPs to make the details of the amplitude more visible (Figure 3). In the previous version, due to incorrect settings, we did not adjust the ordinate spacing when fitting curves of representative wave lines in four groups, resulting in the curves being compressed vertically to the same height. We have now adjusted the curves to be fitted under the same scale bar (shown in the bottom right corner of Figure. 3A). What’s else, we removed the baseline wave of the OPs wave and adjusted the abscissa scale to highlight the N waves and P waves for easy reading (Figure 3F).

(6) Response to recommendation (6):

There are two different Supplementary Figure 1 and no Supplementary Figure 3, resulting in misaligned references to Supplementary Figures 1, 2, and 3 in the text.

Thank you for your careful review of the manuscript. We have reviewed the manuscript again and identified errors in uploading the supplementary figures, which resulted in duplicate Supplementary Figure 1 and the absence of Supplementary Figure 3. We have corrected these issues and realigned the references to Supplementary Figures 1, 2, and 3 in the text to ensure consistency. We appreciate your attention to detail and your reminder to address this issue.

(7) Response to recommendation (7):

There is confusion about the definition of ORL (outer retina layer). In Lines 208-209, ORL was defined as the combined thickness of the rest to the retinal pigment epithelium (RPE). It seems the ONL is included in ORL. But in lines 358-359, 907-908, "the ORL encompassed the region from the inner segment/outer segment (IS/OS) to the RPE". Please make the definition consistent. In addition, it is hard to distinguish the regions marked by the green lines in Fig. 4A (sham image) after Line 902.

Thank you for your careful review of the manuscript. We have addressed the confusion regarding the definition of the outer retinal layer (ORL). The Heidelberg OCT device does not distinguish the layers of the mouse retina well, so we divided it into three broader layers:

(1) Ganglion Cell Complex (GCC) layer, which encompasses RNFL+GCL+IPL.

(2) Middle Retinal Layer, which includes INL+OPL.

(3) Outer Retinal Layer (ORL), which includes ONL+IS/OS+RPE.

We apologize for the inconsistency and have revised the errors in the manuscript and figure legends accordingly. Additionally, we have removed rare domain-specific acronyms and replaced them with more commonly understood abbreviations, as suggested, to avoid confusion.

Furthermore, we have enlarged parts of the OCT images to better display the layers, hoping to meet the readers' requirements and improve clarity. Thank you for your valuable feedback.

(8) Response to recommendation (8):

Figure 4 (Panels H-J, L-M) incorporated with the text (Line 902) differs from the high-resolution version of Figure 4 included later in the manuscript. In Figure 4 (Panels H-J, L-M) merged with the text (Line 902), the quantification of the IPL and INL thickness is incorrect, and the scale bar is inaccurate. However in the high-resolution version of Figure 4 provided later, the thickness of the RNFL+GCL is incorrect.

Thank you for your careful review of the manuscript. The quantification of the IPL and INL thickness in Figure 4 (Panels H-J, L-M) incorporated with the text has been revised to ensure accurate measurements and scale bars (Figure 4 and line 924). The high-resolution version of Figure 4 provided later has been updated to correct the thickness measurements of the RNFL+GCL. We have ensured that the ordinate in the high-resolution version of Figure 4 now correctly represents length units, consistent with the equal proportional conversion used in the integrated text figures.

Thank you for your valuable feedback and for pointing out these errors. We have made the necessary corrections to align the figures accurately with the manuscript.

(9) Response to recommendation (9):

Line 384-386: the statement "Notably, a-waves in ERG and the thickness of the outer retinal layers in both OCT and HE remained unchanged." is not accurate, since a-waves in ERG is not changed in 3 days but changed in 7 days, and the thickness of the outer retinal layers in HE is either not measured or not shown in Figure 4.

Thank you for your careful review of the manuscript. We apologize for this error and have revised it.

We aimed to convey that the amplitude of the a-waves, which represent the function of the photoreceptors, does not show significant variation, which is consistent with the thickness of the outer retinal layer observed in OCT and HE images. Our results indicated that at 7 days post-injury, the amplitude of the a-waves in ERG was statistically different only at stimulus light intensity of 0.3, 3.0 and 10.0 cd.s/m2. In contrast, the b-wave amplitude was reduced by half compared to sham eyes at almost all stimulus light intensities. At the same time, the immunofluorescence staining results of photoreceptor cells showed no significant change at 7-days. Therefore, we consider the change in a-wave amplitudes were not significant compared to the significant decrease in b-wave amplitude. We have clarified this in the revised manuscript.

We also analyzed the thickness of the outer retinal layers in HE and found it to be consistent with OCT results, showing no significant changes (shown in below Author response image 2).

Thank you for your valuable feedback, which has helped improve the accuracy and clarity of our manuscript.

Author response image 2.

Thickness of OPL, ONL, IS/OS+RPE in HE staining. n=3; ns: no significance (p>0.05).

(10) Response to recommendation (10):

Figure 5 and Figure S3: Quantification data from different sections of the same retina should be averaged to represent one single sample (one data point) for statistical analysis. * in images of Fig. 5E, F, I, J is not defined in the figure legend. It would be easier for readers to follow if the GCL, IPL, INL, and OPL were labeled in retinal sections.

Thank you for your careful review of the manuscript and recommendation. We have reperformed the statistical analysis and updated the results in Figure 5 and Figure S3. In the UPOAO experimental eyes, no no significant change in the number of HCs (Calbindin) was observed during the 3-days reperfusion period, while a notable reduction was observed after 7 days (Figure 5). Additionally, we have added the definition of the asterisks (*) in the figure legend to clarify their significance. We have also labeled the retinal layers, including the GCL, IPL, INL, OPL, and ONL, in the images to make it easier for readers to follow and understand the data.

Thank you for helping us improve the clarity and accuracy of our manuscript.

(11) Response to recommendation (11):

Lines 407-409, the statement "which aligns with the a-waves observed in ERG (Figure 3D, E) and the changes seen in the outer retinal layers in OCT (Fig S2C, D)" is confusing. No changes were observed by OCT in Fig S2D.

Thank you for your review and we are sorry about the confusion. The overall trend of the amplitude of the a-wave in ERG at 7-days did not change significantly, which is consistent with the immunofluorescence staining results of the photoreceptor cells. Based on these observations, we consider that the change in the amplitude of the a-wave was not significant. As you pointed out in recommendation 9，since a-waves in ERG were changed in 7-days at the stimulus light intensity of 0.3, 3.0 and 10.0 cd.s/m2, our description on the a-waves in 7-days was not accurate. We have clarified this point in the revised manuscript to ensure it accurately reflects the data presented.

(12) Response to recommendation (12):

In Figure S4, panel C shows lymphocyte-mediated immunity, and panel D shows leukocyte-mediated immunity. Please adjust the figure legend accordingly to reflect the figures.

Thank you for your careful review of the manuscript. We have modified the figure legend of Figure S4.

(13) Response to recommendation (13):

Lines 440-442 state "These results suggested early ischemic processions such as cell migration and potential collateral vessel formation." It is not clear why and how "potential collateral vessel formation" is suggested by Figure 6 and Figure S4. Please clarify this in the text.

Thank you for your careful review of the manuscript and we have deleted this sentence due to insufficient evidence. We have corrected this sentence: "These results suggested that in the early stage of retinal ischemic injury, leukocytes from the microvasculature may infiltrate retinal tissue. More experimental validation will be performed to confirm this hypothesis."(line 448). We will be more cautious in drawing conclusions in the future. Thank you for your reminder.

(14) Response to recommendation (14):

For the figure legend of Figure 6 "In each heatmap, upper box showed the top 10 up-regulated genes, and the below one showed the top 10 down-regulated genes." Is this correct? It appears that the upper box shows the top 10 down-regulated genes, and the lower box shows the top 10 up-regulated genes.

Thank you for your careful review of the manuscript and we have modified the figure legend of Figure 6. In the heatmaps, the upper box showed the top 10 down-regulated genes, and the below one showed the top 10 up-regulated genes (line 977).

(15) Response to recommendation (15):

For the figure legend of Figure 7, the statement 'Data points are from retinal sections of four animals' is incorrect, as these data were obtained from whole retinas instead of retinal sections. Please revise the legend to reflect this accurately. The scale bar was absent in the images of Figure 7. Asterisk in Figure 7H and 7I was not defined.

Thank you for your careful review of the manuscript and we have revised the errors. We have added the scale bar (Figure 7D). The white asterisks in Figure 7H and 7I indicate the activated microglial cells and we have added this definition in the legend of Figure7 (line 981).

(16) Response to recommendation (16):

It would be better to switch the order of Figure S7 and Figure S8 to align with their descriptions in the text.

Thank you for your recommendation and we have switched the order of Figure S7 and Figure S8.

(17) Response to recommendation (17):

The gene names in Figure S8 should be written consistently with those listed in Table S1.

Thank you for your recommendation and we have corrected the gene names.

(18) Response to recommendation (18):

In Figure 9, it is not clear why amacrine cells were not included in the UPOAO model, as amacrine cells were also injured as shown in Figure 5I-L.

Thank you for your careful review of the manuscript and we have added amacrine cells in Figure 9.

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(3) Lee, D., et al., A mouse model of retinal hypoperfusion injury induced by unilateral common carotid artery occlusion. Experimental Eye Research, 2020. 201: p. 108275.

(4) Barthels, D. and H. Das, Current advances in ischemic stroke research and therapies. Biochim Biophys Acta Mol Basis Dis, 2020. 1866(4): p. 165260.

(5) Smith, H.K., et al., Critical differences between two classical surgical approaches for middle cerebral artery occlusion-induced stroke in mice. J Neurosci Methods, 2015. 249: p. 99-105.

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(7) Tinjust, D., H. Kergoat, and J.V. Lovasik, Neuroretinal function during mild systemic hypoxia. Aviat Space Environ Med, 2002. 73(12): p. 1189-94.

(8) Lee, D., et al., Retinal Degeneration in a Murine Model of Retinal Ischemia by Unilateral Common Carotid Artery Occlusion. Biomed Res Int, 2021. 2021: p. 7727648.

(9) Yamamoto, H., et al., Complex neurodegeneration in retina following moderate ischemia induced by bilateral common carotid artery occlusion in Wistar rats. Exp Eye Res, 2006. 82(5): p. 767-79.

(10) Palmhof, M., et al., From Ganglion Cell to Photoreceptor Layer: Timeline of Deterioration in a Rat Ischemia/Reperfusion Model. Front Cell Neurosci, 2019. 13: p. 174.

(11) Adachi, M., et al., High intraocular pressure-induced ischemia and reperfusion injury in the optic nerve and retina in rats. Graefes Arch Clin Exp Ophthalmol, 1996. 234(7): p. 445-51.

(12) Jehle, T., et al., Quantification of ischemic damage in the rat retina: a comparative study using evoked potentials, electroretinography, and histology. Invest Ophthalmol Vis Sci, 2008. 49(3): p. 1056-64.

(13) Hayreh, S.S., H.E. Kolder, and T.A. Weingeist, Central retinal artery occlusion and retinal tolerance time. Ophthalmology, 1980. 87(1): p. 75-8.

(14) Luo, X., et al., Hypoglycemia induces general neuronal death, whereas hypoxia and glutamate transport blockade lead to selective retinal ganglion cell death in vitro. Invest Ophthalmol Vis Sci, 2001. 42(11): p. 2695-705.

(15) Schmid, H., et al., Loss of inner retinal neurons after retinal ischemia in rats. Invest Ophthalmol Vis Sci, 2014. 55(4): p. 2777-87.

(16) Furashova, O. and E. Matthè, Hyperreflectivity of Inner Retinal Layers as a Quantitative Parameter of Ischemic Damage in Acute Retinal Vein Occlusion (RVO): An Optical Coherence Tomography Study. Clin Ophthalmol, 2020. 14: p. 2453-2462.

(17) Pang, Y., et al., CD38 Deficiency Protects Mouse Retinal Ganglion Cells Through Activating the NAD+/Sirt1 Pathway in Ischemia-Reperfusion and Optic Nerve Crush Models. Invest Ophthalmol Vis Sci, 2024. 65(5): p. 36.

(18) Feng, Y., et al., GSK840 Alleviates Retinal Neuronal Injury by Inhibiting RIPK3/MLKL-Mediated RGC Necroptosis After Ischemia/Reperfusion. Invest Ophthalmol Vis Sci, 2023. 64(14): p. 42.

(19) Zeng, S., et al., CREG Protects Retinal Ganglion Cells loss and Retinal Function Impairment Against ischemia-reperfusion Injury in mice via Akt Signaling Pathway. Mol Neurobiol, 2023. 60(10): p. 6018-6028.

(20) Rosenbaum, D.M., et al., The role of the p53 protein in the selective vulnerability of the inner retina to transient ischemia. Invest Ophthalmol Vis Sci, 1998. 39(11): p. 2132-9.

(21) Zhang, Y., et al., Melatonin Alleviates Pyroptosis of Retinal Neurons Following Acute Intraocular Hypertension. CNS Neurol Disord Drug Targets, 2021. 20(3): p. 285-297.

(22) Zhu, J., et al., Protective effects of Erigeron breviscapus Hand.- Mazz. (EBHM) extract in retinal neurodegeneration models. Mol Vis, 2018. 24: p. 315-325.

(23) Wachtmeister, L., Oscillatory potentials in the retina: what do they reveal. Prog Retin Eye Res, 1998. 17(4): p. 485-521.

(24) Cao, W., et al., Dextromethorphan attenuates the effects of ischemia on rabbit electroretinographic oscillatory potentials. Documenta Ophthalmologica, 1993. 84(3): p. 247-256.

(25) Xu, J., et al., Pregabalin Mediates Retinal Ganglion Cell Survival From Retinal Ischemia/Reperfusion Injury Via the Akt/GSK3β/β-Catenin Signaling Pathway. Invest Ophthalmol Vis Sci, 2022. 63(12): p. 7.

(26)Takács, B., et al., Electroretinographical Analysis of the Effect of BGP-15 in Eyedrops for Compensating Global Ischemia-Reperfusion in the Eyes of Sprague Dawley Rats. Biomedicines, 2024. 12(3).

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eLife assessment

The work investigates mechanisms necessary and sufficient for initiating tissue bending in the Cellular Potts Model. The authors emphasize how differences in implicit model assumptions, such as different constraints on cell shape change and cell rearrangement, may explain different outcomes in Cellular Potts Model and Vertex Model simulations. Despite incomplete evidence supporting the major claims due to a rather coarse-grained exploration of the model, the findings are valuable for the biophysics and computational biology communities, and cautions toward greater care in interpretation of model results.

Reviewer #1 (Public Review):

Summary:

Satoshi Yamashita et al., investigate the physical mechanisms driving tissue bending using the cellular Potts Model, starting from a planar cellular monolayer. They argue that apical length-independent tension control alone cannot explain bending phenomena in the cellular Potts Model, contrasting with previous works, particularly Vertex Models. They conclude that an apical elastic term, with zero rest value (due to endocytosis/exocytosis), is necessary to achieve apical constriction, and that tissue bending can be enhanced by adding a supracellular myosin cable. Additionally, a very high apical elastic constant promotes planar tissue configurations, opposing bending.

Strengths:

- The finding of the required mechanisms for tissue bending in the cellular Potts Model provides a natural alternative for studying bending processes in situations with highly curved cells.<br /> - Despite viewing cellular delamination as an undesired outcome in this particular manuscript, the model's capability to naturally allow T1 events might prove useful for studying cell mechanics during out-of-plane extrusion.

Weaknesses:

- The authors claim that the cellular Potts Model (CPM) is unable to achieve the results of the vertex model (VM) simulations due to naturally non-straight cellular junctions in the CPM versus the VM. The lack of a substantial comparison undermines this assertion. None of the references mentioned in the manuscript are from a work using vertex model with straight cellular junctions, simulating apical constriction purely by a enhancing a length-independent apical tension. Sherrard et al and Pérez-González et al. use 2D and 3D Vertex Models, respectively, with a "contractility" force driving apical constriction. However, their models allow cell curvature. Both references suggest that the cell side flexibility of the CPM shouldn't be the main issue of the "contractility model" for apical constriction.<br /> - The myosin cable is assumed to encircle the invaginated cells. Therefore, it is not clear why the force acts over the entire system (even when decreasing towards the center), and not locally in the contour of the group of cells under constriction. The specific form of the associated potential is missing. It is unclear how dependent the results of the manuscript are on these not-well-motivated and model-specific rules for the myosin cable.<br /> - The authors are using different names than the conventional ones for the energy terms. Their current attempt to clarify what is usually done in other works might lead to further confusion.

Reviewer #2 (Public Review):

Summary:

In their work, the Authors study local mechanics in an invaginating epithelial tissue. The work, which is mostly computational, relies on the Cellular Potts model. The main result shows that an increased apical "contractility" is not sufficient to properly drive apical constriction and subsequent tissue invagination. The Authors propose an alternative model, where they consider an alternative driver, namely the "apical surface elasticity".

Strengths:

It is surprising that despite the fact that apical constriction and tissue invagination are probably most studied processes in tissue morphogenesis, the underlying physical mechanisms are still not entirely understood. This work supports this notion by showing that simply increasing apical tension is perhaps not sufficient to locally constrict and invaginate a tissue.

Weaknesses:

Although the Authors have improved and clarified certain aspects of their results as suggested by the Reviewers, the presentation still mostly relies on showing simulation snapshots. Snapshots can be useful, but when there are too many, the results are hard to read. The manuscript would benefit from more quantitative plots like phase diagrams etc.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Satoshi Yamashita et al., investigate the physical mechanisms driving tissue bending using the cellular Potts Model, starting from a planar cellular monolayer. They argue that apical length-independent tension control alone cannot explain bending phenomena in the cellular Potts Model, contrasting with the vertex model. However, the evidence supporting this claim is incomplete. They conclude that an apical elastic term, with zero rest value (due to endocytosis/exocytosis), is necessary in constricting cells and that tissue bending can be enhanced by adding a supracellular myosin cable. Notably, a very high apical elastic constant promotes planar tissue configurations, opposing bending.

Strengths:

- The finding of the required mechanisms for tissue bending in the cellular Potts Model provides a more natural alternative for studying bending processes in situations with highly curved cells.

- Despite viewing cellular delamination as an undesired outcome in this particular manuscript, the model's capability to naturally allow T1 events might prove useful for studying cell mechanics during out-of-plane extrusion.

We thank the reviewer for the careful comments and insightful suggestions.

Weaknesses:

- The authors claim that the cellular Potts Model is unable to obtain the vertex model simulation results, but the lack of a substantial comparison undermines this assertion. No references are provided with vertex model simulations, employing similar setups and rules, and explaining tissue bending solely through an increase in a length-independent apical tension.

Studies cited in a previous paragraph included the simulations employing the increased length-independent apical tension. For the sake of clarity, we added the citation to them as below.

P4L174: “In contrast to the simulations in the preceding studies (Sherrard et al., 2010; Conte et al., 2012; Perez-Mockus et al., 2017; Pérez-González et al., 2021), our simulations could not reproduce the apical constriction”.

We did not copy the parameters of the vertex models in the preceding studies because we also found that the apical, lateral, and basal surface tensions must be balanced otherwise the epithelial cell could not maintain the integrity (Figure 1—figure supplement 1), while the ratio was outside of the suitable range in the preceding studies.

- The apparent disparity between the two models is attributed to straight versus curved cellular junctions, with cells with a curved lateral junction achieving lower minimum energies at steady-state. However, a critical discussion on the impact of T1 events, allowing cellular delamination, is absent. Note that some of the cited vertex model works do not allow T1 events while allowing curvature.

We appreciate the comment and added it to the discussion as suggested.

P12L301: “Even when the vertex model allowed the curved lateral surface, the model did not assume the cells to be rearranged and change neighbors, limiting the cell delamination (Pérez-González et al., 2021).”

P12L311: “Note that the vertex model could also be extended to incorporate the curved edges and rearrangement of the cells by specifically programming them, and would reproduce the cell delamination. That is, we could find the importance of the balanced pressure because the cellular Potts model intrinscally included a high degree of freedom for the cell shape, the cell rearrangement, and the fluctuation.”

- The suggested mechanism for inducing tissue bending in the cellular Potts Model, involving an apical elastic term, has been utilized in earlier studies, including a cited vertex model paper (Polyakov 2014). Consequently, the physical concept behind this implementation is not novel and warrants discussion.

The reviewer is correct but Polyakov et al. assumed “that the cytoskeletal components lining the inside membrane surfaces of the cells provide these surfaces with springlike elastic properties” without justification. We assumed that the myosin activity generated not the elasticity but the contractility based on Labouesse et al. (2015), and expected that the surface elasticity corresponded with the membrane elasticity. Also, in the physical concept, we clarified how the contractility and the elasticity differently deformed the cells and tissue, and demonstrated why the elasticity was important for the apical constriction. We added it to the discussion as below.

P12L316: “In the preceding studies, the apically localized myosin was assumed to generate either the contractile force (Sherrard et al., 2010; Conte et al., 2012; Perez-Mockus et al., 2017; Pérez-Vonzález et al., 2021) or the elastic force (Polyakov et al., 2014; Inoue et al., 2016; Nematbakhsh et al., 2020). However, the limited cell shape in the vertex model made them similar in terms of the energy change during the apical constriction, i.e., the effective force to decrease the apical surface. In this study, we showed that the contractile force and the elastic force differently deformed the cells and tissue, and demonstrated why and how the elasticity was important for the apical constriction.”

- The absence of information on parameter values, initial condition creation, and boundary conditions in the manuscript hinders reproducibility. Additionally, the explanation for the chosen values and their unit conversion is lacking.

We agree with the comment.

For the initial configuration, we added an explanation to Tissue deformation by increased apical contractility with cellular Potts model section in the Results as below.

P4L170: “A simulation started from a flat monolayer of cells beneath the apical ECM, and was continued until resulting deformation of cells and tissue could be evaluated for success of failure of reproducing the apical constriction.”

For the parameter values we added a section “Parameters for the simulations” in the Methods.

For the parameters unit conversion, we did not measure the surface tension and cell pressure in an actual tissue and thus could not compare the parameters to the actual forces. Instead, we varied the parameters and demonstrated that the apical constriction was reproduced with the wide range of the parameter values. We added it to the discussion as below.

P12L310: “It succeeded with a wide range of parameter values, indicating a robustness of the model.”

Reviewer #2 (Public Review):

Summary:

In their work, the authors study local mechanics in an invaginating epithelial tissue. The mostly computational work relies on the Cellular Potts model. The main result shows that an increased apical "contractility" is not sufficient to properly drive apical constriction and subsequent tissue invagination. The authors propose an alternative model, where they consider an alternative driver, namely the "apical surface elasticity".

Strengths:

It is surprising that despite the fact that apical constriction and tissue invagination are probably most studied processes in tissue morphogenesis, the underlying physical mechanisms are still not entirely understood. This work supports this notion by showing that simply increasing apical tension is perhaps not sufficient to locally constrict and invaginate a tissue.

We thank the reviewer for recognizing the importance and novelty of our work.

Weaknesses:

The findings and claims in the manuscript are only partially supported. With the computational methodology for studying tissue mechanics being so well developed in the field, the authors could probably have done a more thorough job of supporting the main findings of their work.

We thank the reviewer for the careful assessment and suggestions. However our simulation was computationally expensive, modeling the epithelium in an analytically calculable expression requires a lot of work, and it is beyond the scope of the present study.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) Reference line 648: Correct the author's name (Pérez-González).

We thank the reviewer and corrected the reference.

(2) "Pale" colors are challenging to discern.

We updated the figures.

(3) Figure 1j: What does the yellow color in the cellular junction represent?

We used the apical lateral site colored yellow in Fig. 1e-f’ to simulate the effect of the adherens junction. We updated the figure legend.

(4) Figure 2c - left: Why is there a red apical junction?

Our simulation model marked the apical junction in the initial configuration and updated the marking based on connectedness to surrounding other site marked as apical in the same cell. But when a cell was once delaminated and lost its apical junction, any surface site not adjacent to other epithelial cells were marked as basal junction because they were not adjacent to the apical junction.

We added it to Cellular Potts model with partial surface elasticity section in the Methods as below.

P17L430: “To simulate the differential phyisical properties of the apical, lateral, and basal surfaces, the subcellular locations are marked automatically, and the marking is updated during the simulation. In each cell, sites adjacent to different cells but not to the medium are marked as lateral.

At the initial configuration, sites adjacent to the apical ECM are marked as apical, and during the simulation, sites adjacent to medium and other apical sites in the same cell are marked as apical.

Rest of sites which are adjacent to medium but not marked as apical are marked as basal.

Therefore, once a cell is delaminated and loses its apical surface, afterwards all sites in the cell adjacent to the medium are marked as basal even if it is adjacent to the apical ECM or the outer body fluid.”

(5) Figure 4a: The snapshots are not in a steady state but in the middle of deformation. Is the time the same for all snapshots? The motivation to change P_0a is related to endocytosis. However, this could be achieved by decreasing P_0a to a non-zero value. Here, in the more drastic limit, the depth (a measure of bending) is very slight, approximately half of a cell size. What physically limits further invagination? Is it the number of cells or the range of parameters under study?

The time length was the same for simulations in each figure, and we add it to Parameters for the simulations section in Method as below.

P18L466: “In each figure, snapshots of the simulations show deformation by the same time length unless specified.”

For P_0a, the reviewer is correct and the iterated ratcheting may decrease P_0a step by step instead of making it 0 immediately. Still, with P_a0 >0, the energy function and its derivative are both increasing with respect to the apical width as long as P_a > P_a0, and thus the apical shrinkage would be synchronized, even though the deformation would be smaller. We also run simulations by decreasing P_0a to 0.6 times the initial P_a, and observed smaller deformation as expected. On the other hand, the non-zero P_0a made the invagination deeper when it was combined with the effect of surrounding supracellular myosin cable, maybe due to a resistance of the apical surface against compression. One of the novel and important finding in this study is the synergetic effect of the elasticity-based apical constriction and the surrounding supracellular myosin cable. To demonstrate that the deep invagination was not due to the apical surface resistance against the compression, we showed the simulations with P_a0 = 0.

For the conditions for further invagination, it may include the number of cells, a ratio between the cell height and width (Figure 5—figure supplement 1), interaction with ECM (Figure 5—figure supplement 2), etc. For the parameter, there might be an upper limit (Figure 4). We did not test the number of cells because of its computational cost. Among the conditions we tested, we found the planar compression by surrounding supracellular myosin the most influential rather than the mechanical property of apically constricting cells themselves.

How each condition and parameter contributes to the invagination shall be studied in future. We added it to the conclusion as below.

P15L395: “The depth, curvature, and speed of the invagination might be influenced by the cell shape, configuration, and parameters, and how each condition contributes to the invagination shall be studied in future.”

(6) Figure 6b: What does the cell-surface color represent? If the idea was to represent junction tension, it would be clearer to color the junctions only.

The junction tension may vary differently in different situations. For example, T1 transition is accompanied by enriched myosin along a shrinking cell-cell junction, and the junction bears higher tension, but other junctions of the same cell do not and thus the cell does not decrease its apical surface. In chick embryo neural tube closure, the junction tension is also polarized, and the cells shrink the apical surface along medial-lateral axis, driving the apical constriction (Nishimura et al., 2012, doi:10.1016/j.cell.2012.04.021). In the case of Drosophila embryo tracheal invagination, the cells shrank their apical surface isotropically (Figure 6a). If the junction tension was responsible for the shrinkage, all junctions of the cell must bear higher tension. Based on this assumption, the junction tension was averaged in each cell to check if the tracheal cells bore the higher average tension than surrounding cells.

We also plotted stress tensor and calculated nematic order to check if there was radial or encircling tension alignment in the tracheal pit, but there was not.

(7) Figure 6c: What does the junction color represent here?

The junction color represent the relative junctional tension. We updated the figure legend.

(8) Figure 6d-e: It is challenging to understand which error bar corresponds to each dataset.

We updated the figure.

(9) What is the definition of relative pressure?

The geometrical tension inference method assumes that the tissue is in mechanical equilibrium and a sum of the junctional tensions and cell pressures pulling/pushing a vertex (tricellular junction) is 0. Therefore the calculated tensions and pressures are proportional to each other but not absolute values. We added it to the 3D Bayesian tension inference section of Methods as below.

P24L567: “Since Equation 13 and Equation 14 only evaluate the balance among the forces, it cannot estimate an absolute value but a relative value of the tension and pressure.”

(10) In the main text, it is mentioned that a large Es (apical elastic constant) leads to flat surfaces, avoiding bending, but the abstract says "strong apical surface tension," which, according to the rest of the text, would seem to be J_apical. Clarification is needed.

The surface tension includes both of the surface contractility and the surface elasticity.

We added it to Extended cellular Potts model to simulate epithelial deformations section in the Results as below.

P3L122: “Note that in some studies the tension and the contractility are considered as equivalent, but they are distinguished in this study.”

and

P4L151: “The energy H included only the terms of the contact energy (Equation 1) and the area constraint (Equation 5), but the surface elasticity (Equation 2) nor (Equation 3) was not included, and thus the surface tension was determined by the contact energy.”

Reviewer #2 (Recommendations For The Authors):

(1) The model used is rather specific and it is rather confusing whether the issue is in the methodology or fundamental biophysics of apical constriction. For instance, one of the main narratives of the manuscript is that the Cellular Potts model better predicts apical constriction and tissue invagination than the vertex model. As I understand it, and as the authors state in p7 (line 210), "the difference between the vertex model and the cellular Potts model results was due to the straight lateral surface...". I assume that if apical constriction and tissue invagination were modelled with a vertex model with curved edges, while also allowing for cell rearrangements out of the tissue plane (some sort of epithelium-to-mesenchyme transition), the vertex model would yield exactly the same results as in the authors' cellular Potts model. If my understanding is correct, the authors should change the narrative of their manuscript and focus more on the comparison of a model with flat vs. curved edges, with "contractility" vs. "surface elasticity", with patterned apical contractility vs. non-patterned contractility (see my comment in point 2 below)... and not on comparison between CPM and VM.

We appreciate the comments. The reviewers is correct that the vertex model can include the curved edges and the cell rearrangement, and it would reproduce the result of our cellular Potts model simulations. For the cellular Potts model, there was no need to specifically design how much the cell surface could be curved in a large arc, zigzag, or other shape, and that enabled us to find the conditions of delamination and bending.

We added it to the discussion as below.

P12L311: “Note that the vertex model could also be extended to incorporate the curved edges and rearrangement of the cells by specifically programming them, and would reproduce the cell delamination. That is, we could find the importance of the balanced pressure because the cellular Pott’s model intrinscally included a high degree of freedom for the cell shape, the cell rearrangement, and the fluctuation.”

(2) About physics... and I think this is a really important point: one of the observations in the model was that in the "contractilty" model, only "edge cells" shrank its apical surface, while inner cells remained quadrilateral. Related to this, the authors say that one of the requirements for proper apical constriction is a mechanism that "simulataneously shrinks the apical surface among cells in a cluster". What would happen if the authors assumed patterned contractility, meaning that cells in the center of the cluster would be most apically-contractile, while those further away from the center, would not be contractile? Features like this were investigated in studies of ventral-furrow invagination [see, for instance, Spahn and Reuater PLOS ONE (2013) and Rauzi et al. Nat Commun (2015)-Fig. S13d].

We thank the reviewer for the critical comment, and ran simulations with the patterned apical contractility. The apical contractility following a gradient of parabola shape succeeded in the simultaneous apical shrinkage. However, it was weak against fluctuations and the cells were delaminated by chance.

We added it to Apical constriction by modified apical elasticity section in the result as below.

P9L252: “We also tested another model for the simultaneous apical shrinkage, a gradient contractility model (Spahn and Reuter, 2013; Rauzi et al., 2015). If the inner cells bear higher apical surface contractility than the edge cells, that inner cells may shrink their apical surface. To synchronize the apical shrinkage, the apical contractility must follow a parabola shape gradient. Even though the gradient contractility enabled the cells to shrink the apical surface simultaneously, often some of the cells shrank faster than neighbors and were delaminated by chance (Figure 4—figure Supplement 1).”

(3) The quality of the figures should be improved. Especially, Figure 3 and the related explanation in lines 183-192. This explanation is way too complicated and it is not clear what Figure 3c shows. For instance: if the arrows are indeed showing contractile forces (as written in the caption) then they are not illustrated correctly, but should be tangential to the cell membrane.

We updated the figure.

(4) The figures mostly show steady-state cross-sections from simulations. I miss a more dedicated study with model parameters being varied through wider ranges and some phase diagrams being shown etc. Also, some results could probably be supported by analytic calculations. For instance, the condition for stability (discussed in p4 lines 145-151), cells' preferred aspect ratio, cells' preferred "wedgeness" i.e., local curvature etc... I am sure some of these, if not all, could be calculated analytically and then these analytic results could help to interpret the phase diagrams.

For the simulation results shown in the figures, we were not sure if the simulations results were in a steady state or not. We added it to Tissue deformation by increased apical contractility simulated with cellular Potts model section in the Results as below.

P4L170: “A simulation started from a flat monolayer of cells beneath the apical ECM, and was continued until resulting deformation of cells and tissue could be evaluated for success of failure of reproducing the apical constriction.”

For the ranges of parameters, we ran the simulation in wider range and showed results from sub-range. We added it to Parameters for the simulations section in Methods as below.

P18L464: “The parameters were varied in a range, and the figures showed simulations with parameter values within a sub-range so that the results showed both success and failure in a development of interest.”

For the analytical calculations, the Figure 3f shows a kind of phase diagram for shapes of a single cell. To clarify this, we rephrased “map of cell shapes” to “Phase diagram of cell shapes” in the figure legend, and added an explanation to the Results section as below.

P6L207: “For the analysis of the cell shape in motion, we plotted a phase diagram for shapes of a single cell (Figure 3f).”

For the analytical evaluation of the cellular Potts model simulations, there was a study doing similar but it concerned a cell of isotropic shape in a steady state (Magno et al., 2015, doi:10.1186/s13628-015-0022-x). Also, our simulation framework is computationally expensive and we could not vary the parameters in fine resolution. Therefore we could not include it in this study.

(5) I am not sure about the terminology "contractility" vs. "elasticity". In Farhadifar et al. (2007) "contractility" is described by a squared apical-perimeter energy term, while in this work, the authors describe it by a surface-energy-like term.

In general, elasticity is the ability of a material to resist against deformation and to return to its original shape/size. In Farhadifar et al. (2007), the cell apical area was assigned the area elasticity in this meaning. For the contractility, it is the ability to decrease the size/length, and thus it could be either expressed in linear or quadratic dependent on the modeling. In this study, we assumed cell-cell/cell-ECM adhesion and myosin activity to generate the surface contractility, and thus employed the linear expression. In Farhadifar et al. (2007) it was described as a line tension.

We used the terms surface ‘elasticity’ and ‘contractility’ as distinctive elements composing the surface ‘tension’. We added it Extended cellular Potts model to simulate epithelial deformations section in the Results as below.

P3L122: “Note that in some studies the tension and the contractility are considered as equivalent, but they are distinguished in this study.”

(6) It is not entirely clear what are apical, basal, lateral, and cell "perimeters". This is a 2D model, so I assume all P-s are in fact interface lengths. In either case, this needs to be explained more clearly.

We updated the explanation in Extended cellular Potts model to simulate epithelial deformations section in the Results as below.

P3L111: “The cell's perimeter was partitioned automatically based on adjacency with other cells, and it was marked as apical, lateral, basal. Also, apico-lateral sites were marked as a location for the adherens junction. This cell representation also cast the vertical section of the cell. Therefore an area of the cell corresponded with a body of the cell, and a perimeter of the cell corresponded with the cell surface. Likewise the apical, lateral, and basal parts of the perimeter corresponded with the apical surface, cell-cell interface, and the basal surface of the cell respectively.”

(7) The term H_{mc} is not clear at all. Why is this term called potential energy? What is U(i)? What is the exact biophysical interpretation of this term in 2D vs 3D?

In 3D, the supracellular myosin cable is formed encircling the cells deformed by the apical constriction. Shrinking of the supracellular myosin cable makes the circle small, and it moves the cable toward the center of the circle. To simulate this motion of the supracellular myosin cable in the 2D cross section, we assigned the force exerted on the adherens junction of the boundary cells pulling toward the center, and because the force is relative to the position of the adherens junction and the center, it was expressed by the potential energy in the simulation.

We updated Extended cellular Potts model to simulate epithelial deformation section in Results and Cellular Potts model with potential energy section in Methods as below.

P4L140: “The potential energy was defined by a scalar field which made a horizontal gradient decreasing toward the center,”

and

P17L449: “In 3D, tension on a circular actomyosin cable would shrink the circle, and the shrinkage would pull the cable toward the center of the circle. In 2D cross section, the cable is pulled horizontally toward the middle line.”

(8) Highten->increased

We updated the text.

(9) "It seems natural to consider that the myosin generates a force proportional to its density but not to the surface width nor the strain". This sentence should be supported by a reference. Also, if the force is proportional to myosin density, then it must depend on surface width, since density, I assume, is the number of motors per area.

For the myosin density and generated force, in all preceding studies cited in this manuscript and others in the extent of our knowledge, the myosin and actin filaments density visualized by staining or labeling had been assumed relevant to the generated contractility without references. Therefore it might be well established and shared assumption.

For the independence from the surface width and strain, the review comment is correct, but the results would be the same. If we presumed that the number of motors on the apical surface was constant in a cell during the apical constriction, then the density would increase when the apical surface was contracted, and thus it would make the apical contractility more unbalanced and promote the delamination. We added it to the results and discussion as below.

P4L166: “For the sake of simplicity, we ignored an effect of the constriction on the apical myosin density, and discussed it later.”

P14L328: “In our model, for the sake of simplicity, we ignored an effect of the constriction on the apical myosin density. If we presumed that the apical myosin would be condensed by the shrinkage of the apical surface, it would increase the apical tension in the shrinking cell and is expected to promote the cell delamination further. Therefore it would not change the results.”

Reviewing Editor (Recommendations For The Authors):

Please note also the following excerpts from discussions amongst the reviewers and the Reviewing Editor:

Regarding Reviewer #2's Point 2:

I believe the authors have assumed patterned contractility in their simulations, and this is shown by the "pale blue" cell color (see also lines 162-163). However, as Reviewer #2 points out in their point 2), the pale colors are very hard to see and therefore easy to miss.

We updated figure coloring and also add the gradient pattern of contractility.

Regarding Reviewer #2's point 5:

It is indeed unconventional to call the "J" terms contractility, they are usually called contact energy or adhesive energy.

In this study, we included both of the contact energy of cell-cell/cell-ECM adhesion and actomyosin activity in the surface contractility, and used the “J” term as it was conventional in the cellular Potts model.

On the other hand, due to the parameters chosen for J_apical and J_basal in the pale blue cells, the apical membrane area will tend to shrink and the basal membrane will tend to enlarge. Because the lateral membrane energy J_lateral is constant among all cells (I think?), this will effectively drive cells to apically contract in the center.

That expectation was an initial motivation of our study, but we found that the differential J alone could not drive the cells to apically contract in the center.

I agree that extra clarification by the authors would be very helpful here.

Reviewer #2:

Regarding the patterned contractility: indeed, I missed this point (the pale blue region is really poorly visible).

Nevertheless, it seems that contractility in the authors' model changes in a step-like fashion.

[...] There may be important differences between furrowing under step-like patterning profile versus smooth "bell-like" patterning (see Supplementary Figure 13 in Rauzi et al. Nat Commun 2015). In particular, in the case of a step-like patterning, [there are] constrictions of side cells (similar to what the authors in this manuscript report), whereas in the bell-like patterning, [...] such side constrictions [do not occur].

As replied to the reviewer #2 comment (2), we added the simulations with gradient-pattern contractility.

eLife assessment

This important study presents the structure of human heparan-alpha-glucosaminide N-acetyltransferase (HGSNAT) in the acetyl-CoA bound state, providing the first description of the architecture of this family of integral membrane enzymes, and revealing the mode of acetyl-CoA binding. The structural work is convincing, with a high resolution and isotropic single-particle cryoEM map and an atomic model that is well-justified by the density map, with strong density for the acetyl-CoA ligand. However, experimental support for the molecular mechanism of the HS acetylation reaction and the impact of disease-causing mutations is incomplete. This work will be of interest to biochemists and structural biologists studying the structure and function of integral membrane enzymes, as well as those interested in genetic diseases resulting from mutations in this family of enzymes, such as mucopolysaccharidosis IIIC (MPS III-C).

Author response:

The following is the authors’ response to the original reviews.

We extend our sincere gratitude to the reviewers for their constructive feedback and valuable suggestions, which have significantly contributed to enhancing the quality of our work. In response to the comments, we have meticulously revised our manuscript with the following updates:

(1) New Data Inclusion: We have incorporated new immunofluorescent staining images, FACS analysis of monocytes, and single-cell RNA sequencing (scRNAseq) expression analysis focusing on genes related to IFNGR, as well as T cell memory subsets (Trm, Tcm, and Tem).

(2) Comparative Analysis: We have conducted a comparative analysis between the active vitiligo dFBs and the ACD pAd (r5) identified in our study, which provides further insight into the immune response mechanisms.

(3) Discussion Expansion: We have expanded the discussion to include the role of tissue-resident memory (Trm) T cells in our model and have addressed the limitations of our animal model and in vitro studies.

(4) Supplemental Material: As requested by the reviewers, we have provided four new supplemental tables (Table S2 ~ S5) and specific information for antibodies used in our study.

Please see our Point-to-Point Responses to Reviewers' comments below:

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this manuscript, Liu et al. used scRNA-seq to characterize cell type-specific responses during allergic contact dermatitis (ACD) in a mouse model, specifically the hapten-induced DNFB model. Using the scRNA-seq data, they deconvolved the cell types responsible for the expression of major inflammatory cytokines such as IFNG (from CD4 and CD8 T cells), IL4/13 (from basophils), IL17A (from gd T cells), and IL1B from neutrophils and macrophages. They found the highest upregulation of a type 1 inflammatory response, centering around IFNG produced by CD4 and CD8 T cells. They further identified a subpopulation of dermal fibroblasts that upregulate CXCL9/10 during ACD and provided functional genetic evidence in their mouse model that disrupting IFNG signaling to fibroblasts decreases CD8 T cell infiltration and overall inflammation. They identify an increase in IFNG-expressing CD8 T cells in human patient samples of ACD vs. healthy control skin and co-localization of CD8 T cells with PDGFRA+ fibroblasts, which suggests this mechanism is relevant to human ACD. This mechanism is reminiscent of recent work (Xu et al., Nature 2022) showing that IFNG signaling in dermal fibroblasts upregulates CXCL9/10 to recruit CD8 T cells in a mouse model of vitiligo. Overall, this is a very wellpresented, clear, and comprehensive manuscript. The conclusions of the study are mostly well supported by data, but some aspects of the work could be improved by additional clarification of the identity of the cell types shown to be involved, including the exact subpopulation discovered by scRNA-seq and the subtype of CD8 T cell involved. The study was limited by its use of one ACD model (DNFB), which prevents an assessment of how broadly relevant this axis is. The human sample validation is slightly circumstantial and limited by the multiplexing capacity of immunofluorescence markers.

Strengths:

Through deep characterization of the in vivo ACD model, the authors were able to determine which cell types were expressing the major cytokines involved in ACD inflammation, such as IFNG, IL4/13, IL17A, and IL1B. These analyses are well-presented and thoughtful, showing first that the response is IFNG-dominant, then focusing on deeper characterization of lymphocytes, myeloid cells, and fibroblasts, which are also validated and complemented by FACS experiments using canonical markers of these cell types as well as IF staining. Crosstalk analyses from the scRNA-seq data led the authors to focus on IFNG signaling fibroblasts, and in vitro experiments demonstrate that CXCL9 and CXCL10 are expressed by fibroblasts stimulated by IFNG. In vivo functional genetic evidence demonstrates an important role for IFNG signaling in fibroblasts, as KO of Ifngr1 using Pdgfra-Cre Ifngr1 fl/fl mice, showed a reduction in inflammation and CD8 T cell recruitment.

Weaknesses:

(1) The use of one model limits an understanding of how broad this fibroblast-T cell axis is during ACD. However, the authors chose the most commonly employed model and cited additional work in a vitiligo model (another type 1 immune response).

We thanks the reviewer for pointing out this limitation. Although the DNFB-elicited ACD model is the most commonly used animal model for ACD, our study is limited by the use of only one type 1 immune response model. We have now added new data (Figure 5-figure supplement 1A) showing that the active ACD pAd (r5) and the active IFNγ-responsive vitiligo dFBs (Xu et al., 2022) are enriched with a highly similar panel of IFNγ-inducible genes. Future studies are still needed to determine whether this fibroblast-T cell axis may be broadly applied to other ACD models or to other type-1 immune response-related inflammatory skin diseases.

(2) The identity of the involved fibroblasts and T cells in the mouse model is difficult to assess as scRNA-seq identified subpopulations of these cell types, but most work in the Pdgfra-Cre Ifngr1 fl/fl mice used broad markers for these cell types as opposed to matched subpopulation markers from their scRNA-seq data.

Thanks for the reviewer's constructive comments. To better showcase the dWAT layer where PDGFRA+ pAds are enriched, we have included new histological staining and PLIN1 (adipocyte marker) in new Figure 4 - figure supplement 1F-G. As shown in Figure 4 - figure supplement 1G, the PLIN1+ dWAT layer is located in the lower dermis right above the cartilage layer.  In Figure 4-figure supplement 1I and J, we have shown that phosphor-STAT1 (pSTAT1), a key signaling molecule activated by IFNγ, was detected primarily in PDGFRA+Ly6A+ pAds in the lower dermis where dWAT is located. In addition, we have now included new data showing that the pAd (dFB_r5) cluster preferentially expressed the highest levels of both Ifngr1 and Ifngfr2 among all dFB subclusters (new Figure 5 - figure supplement 1B). Furthermore, we have included new co-staining data showing that CXCL9 largely co-localized with ICAM1(new Figure 4 - figure supplement 1K), a marker for committed pAds (Merrick et al., 2019), in the reticular dermis and dWAT region of the ACD skin, further confirming that CXCL9 is specifically induced in the pAd subset of dFBs. Additionally, we included new staining data showing that ACD-mediated induction of CXCL9 in ICAM1+ dFBs were largely suppressed upon targeted deletion of Ifngr1 in Pdgfra+ dFBs (new Figure 6 - figure supplement 1D-E).

(3) Human patient samples of ACD were co-stained with two markers at a time, demonstrating the presence of CD8+IFNG+ T cells, PDGFRA+CXCL10+ fibroblasts, and co-localization of PDGFRA+ fibroblasts and CD8+ T cells. However, no IF staining demonstrates co-expression of all 4 markers at once; thus, the human validation of co-localization of CD8+IFNG+ T cells and PDGFRA+CXCL10+ fibroblasts is ultimately indirect, although not a huge leap of faith. Although n=3 samples of healthy control and ACD samples are used, there is no quantification of any results to demonstrate the robustness of differences.

Thanks for the reviewer’s constructive comments. We have shown that PDGFRA colocalizes with CXCL10, in the dermal micro-vascular structures, where CD8+ T cells infiltrate around PDGFRA+ dFBs. We are sorry that due to technical issues (antibody compatibility), we cannot provide the four color co-staining as suggested by the reviewers. In order to demonstrate the robustness and reproducibility of the staining presented, we have now supplemented 4 independent images for both Fig. 7A and Fig. 7E in the updated Figure 7-figure supplement 1A-B.

Reviewer #2 (Public Review):

Summary:

The investigators apply scRNA seq and bioinformatics to identify biomarkers associated with DNFB-induced contact dermatitis in mice. The bioinformatics component of the study appears reasonable and may provide new insights regarding TH1-driven immune reactions in ACD in mice. However, the IF data and images of tissue sections are not clear and should be improved to validate the model.

Strengths:

The bioinformatics analysis.

Weaknesses:

The IF data presented in 4H, 6H, 7E and 7F are not convincing and need to be correlated with routine staining on histology and different IF markers for PDGFR. Some of the IF staining data demonstrates a pattern inconsistent with its target.

We are sorry for the confusion, because 4H and 6H are staining on mouse skin sections, and 7E and 7F are staining on human skin sections, therefore the patterns of PDGFRA+ dFBs appeared inconsistent between species. As shown in Fig. 4H, in mouse skin, PDGFRA+CXCL9/10+ dFBs are located between the lower reticular dermis and dWAT region, where preadipocytes are located (Sun et al., 2023). To better showcase the dWAT layer where PDGFRA+ pAds are enriched, we have included new histological staining and PLIN1 (adipocyte marker) in new Figure 4 - figure supplement 1F-G. As shown in Figure 4 - figure supplement 1G, the PLIN1+ dWAT layer is located in the lower dermis right above the cartilage layer. Furthermore, we have included new co-staining data showing that CXCL9 largely co-localized with ICAM1(new Figure 4 - figure supplement 1K), a marker for committed pAds (Merrick et al., 2019), in the reticular dermis and dWAT region of the ACD skin, further confirming that CXCL9 is specifically induced in the pAd subset of dFBs.   

As shown in Fig. 7E, in human skin, PDGFRA+CXCL10+ dFBs are located within the microvascular structures located at the dermal-epidermal junction (DEJ) region, where mesenchymal stem cells are enriched (Russell-Goldman & Murphy, 2020). We have included the corresponding HE histological staining image for Fig. 4H in new Figure 4-supplement 1F. Histological staining for Fig. 6H is the HE staining image in Fig. 6F. The histological staining for Fig. 7E and 7F is shown by Masson’s trichrome staining shown in Fig. 7C (a three-colour histological staining).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Major comments:

(1) While the focus on fibroblast and T cell interactions and overall biological findings regarding these interactions (IFNG - CXCL9/10 - CXCR3) is sound, it is slightly confusing about which exact subpopulations of these cells are involved in ACD pathogenesis as both scRNA-seq and IF are used but very broad markers are used for IF. Regarding fibroblasts, the scRNA-seq identifies the pAd (r5) cluster of fibroblasts as the main producer of CXCL9/10. However, the expression of IFNGR1 was not shown for this subpopulation as well as for other fibroblast subpopulations. Figure 6C shows IFNGR1 staining in the Ifngr1 fl/fl control mice which appears quite broad. With the seemingly broad expression of IFNGR1, why is it that only a subpopulation of fibroblasts upregulate CXCL9/10? Is there a specific location of these pAd fibroblasts that help drive this IFNG response? Please show the expression of Ifngr1 in the fibroblast scRNA-seq data.

Thanks for the reviewer’s constructive comments. We have now included new data showing that the pAd (dFB_r5) cluster preferentially expressed higher levels of both Ifngr1 and Ifngfr2 among all dFB subclusters (new Figure 5 - figure supplement 1B). In addition, we included new co-staining data showing that CXCL9 largely co-localized with ICAM1, a marker for committed pAds (Merrick et al., 2019), in the reticular dermis and dWAT region of the ACD skin, further confirming that CXCL9 is specifically induced in the pAd subset of dFBs.

(2) Regarding T cells, it is slightly confusing regarding what role the fibroblast-produced CXCL9/10 plays on T cell migration vs. activation. This is mainly because in vitro work focuses on T cell activation, while in vivo work seems to mainly assess T cell migration into the tissue. The in vivo studies have nicely shown that CD8 T cells are the main cell type affected by Ifngr1 iKO (i.e., a reduction of these cells), but T cell activity in vivo is not assessed (in the form of IFNG production). I have the following related questions:

a. Authors do not discuss whether T cells involved in ACD in their model are tissue-resident memory T cells (Trm) or whether these are recruited from circulation. This may be possible to assess via additional analysis of the scRNA-seq data (looking for expression of Trm markers). 

Thanks for the reviewer’s constructive comments. We have now included new data showing the expression of marker genes of various memory T cells in various T cell subclusters (new Figure 2 - figure supplement 1C-D). Antigen-specific CD8 or CD4 memory T cells can be classified into CD62hi/CCR7hi/CD28hi/CD27hi/CX3CR1lo central memory T cells (Tcm), CX3CR1hi/Cd28hi/Cd27lo/CD62lo/CCR7lo effector memory T cells (Tem), and CD49ahi/CD103hi/ CD69hi/BLIMP1hi tissue-resident memory T cells (Trm) (Benichou, Gonzalez, Marino, Ayasoufi, & Valujskikh, 2017; Cheon, Son, & Sun, 2023; Mackay et al., 2013; Martin & Badovinac, 2018; Park et al., 2023). We observed that in ACD skin, CD4+ and CD8+ T cells predominantly expressed marker genes associated with Tcm including Cd28, Cd27, Ccr7, and S1pr1/Cd62l. In contrast, marker genes associated with Tem (Cx3cr1) and Trm (Itga1/Cd49a, Itgae/Cd103, Cd69 and Prdm1/Blimp1, Cd127/Il7r) were only scarcely expressed in these αβ T cells, suggesting that ACD predominantly triggers a central memory T cell response in the skin.

Furthermore, this hypothesis is supported by new lymph node gene expression results. We showed that the expression of Ifng, but not Il4 or Il17a, was rapidly induced in skin draining lymph nodes at 24 hours after ACD elicitation (new Figure 1-figure supplement 1H). This suggests a robust and systemic activation of type 1 memory T cell response in the early stage of ACD, and the migration of these lymphatic memory T cells to the skin may contribute to the exacerbation of skin inflammation.

b. Authors have focused on CXCR3 axis involvement in IFNG production (Figures 5G-H) without assessing the presumed migratory role of this axis. Presumably, CD8 T cells are recruited to the skin via the CXCL9/10-CXCR3 axis, but this would be important to clarify given other work that has demonstrated Trm involvement in ACD. Authors should at least discuss how their model and findings support, refine, or even contradict the current paradigm of Trm involvement in ACD (Lefevre et al., 2021; PMID: 34155157).

We are grateful for the constructive feedback provided by the reviewer. CXCR3 is a chemokine receptor on T cells and not only plays a pivotal role in the trafficking of type 1 T cells, but also is required for optimal generation of IFNG-secreting type 1 T cells in vivo (Groom et al., 2012). Our in vitro study is limited by only focusing on CXCL9/10-CXCR3 axis involvement in IFNγ production without studying its role in driving T cell migration. We have now addressed this limitation in the discussion section.

In the murine model of ACD, the initial sensitization phase involves exposing mouse skin to a high dose of DNFB to prime effector T cells in lymphoid organs, and this is followed by a later challenge/elicitation phase, during which the mice are re-exposed to a lower dose of DNFB in a different area of the skin, distal from the original sensitization site (Manresa, 2021; Vocanson, Hennino, Rozieres, Poyet, & Nicolas, 2009). Our updated analysis of the expression of marker genes associated with central memory T cells (Tcm), effector memory T cells (Tem), and tissue-resident memory T cells (Trm), as presented in the revised Figure 2-figure supplement 1C-D, indicates that indicate that the type-1 inflammation observed upon ACD elicitation is predominantly driven by memory T cells recruited from lymphoid organs, rather than by skin resident memory T cells. We have read the reference provided by the reviewer along with a few other related studies indicating that Trm is involved in ACD. We found that these studies performed the elicitation phase on the same skin area where the initial sensitization is conducted, and only when it results in a rapid allergen-induced skin inflammatory response, that is primarily mediated by IL17A-producing and IFNγ-producing CD8+ skin resident memory T cells (Gadsboll et al., 2020; Murata & Hayashi, 2020; Schmidt et al., 2017; Wongchang et al., 2023). These studies suggest that Trm cells establish a long-lasting local memory during the initial sensitization, and upon re-exposure to the hapten in the same skin area, these site-specific Trm cells can rapidly contribute to a robust type-1 skin inflammatory response. Therefore, a robust involvement of Trm in ACD requires a repeated exposure of the same hapten to the same skin area. We have now added related discussion in the discussion section.

c. While it may be difficult to assess given reduced numbers of CD8 T cells in the Ifngr1 iKO, is the CXCL9/10-CXCR3 axis affecting IFNG production by T cells in vivo?

Yes, we have shown in Fig. 6G that ACD-mediated induction of Ifng was significantly suppressed in the Ifngr1-iKO mice compared to the control mice.

(3) The authors cite prior work (Xu et al. Nature 2022) that demonstrated a similar mechanism for fibroblasts in recruiting vitiligo-inducing T cells. Are the pAd (r5) cluster of fibroblasts similar to the fibroblast subpopulation that drives vitiligo?

The study on mouse model of vitiligo (Xu et al. Nature 2022) did not perform single-cell RNAseq of the vitiligo mouse skin. Instead, they conducted RNAseq analysis on the sorted PDGFRA+ dFBs. Therefore, we cannot directly compare our pAd (r5) cluster with the fibroblast subpopulation that drives vitiligo. Nevertheless, by utilizing a Venn diagram to compare the top 100 lFNγ signaling dependent genes upregulated in the active vitiligo mouse dFBs and the top 100 genes enriched in our ACD pAd (dFB_r5) cells, we identified 29 commonly upregulated genes between the two conditions (Figure 5-figure supplement 1A). Furthermore, all these 29 genes were among the top IFNγ-inducible genes in primary dFBs. These shared genes include CXCL9, CXCL10, and several other downstream targets of IFNγ signaling, such as B2M, BST2, CD274, as well as the GBP family members GBP3, GBP4, GBP5, GBP7, and additional genes like H2-K1, H2-Q4, H2-Q7, H2-T23, IFIT3, ISG15, and STAT1. This result suggests that the pAd (dFB_r5) cells possess a common IFNγ-pathway gene signature with the active vitiligo mouse dFBs, indicating a potential overlap in molecular pathways.

(4) The authors should include bulk RNA-seq data from fibroblast stimulation (Figure 5b) at a minimum in the GEO submission. They should ideally include the differentially expressed genes in a supplementary table.

Thanks for the reviewer’s constructive comments. We have now included the raw FPKM file for the bulk RNAseq data shown in Fig. 5 in Supplemental Table S3, and the list for differentially expressed genes in Supplemental Table S4.

(5) The authors state that human sample stainings were n = 3 per group for healthy control and ACD (Figure 7), but no quantification or statistical testing is provided to demonstrate significant differences in findings such as co-localization of fibroblasts and T cells, IFNG+CD8+ T cells, etc.

Thanks for the reviewer’s constructive comments. We have now supplemented 4 independent images for both Fig. 7A and Fig. 7E in the new Figure 7-figure supplement 1A-B to demonstrate the robustness and reproducibility of the staining presented.

Minor comments:

(1) Figure 1G, possible typos, Il14 and Il11b are on the violin plots when I believe authors meant Il4 and Il1b.

Thank a lot for pointing out these typos. We have now made the correction in the updated manuscript figure 1.

(2) The authors label cluster 27 as neutrophils based on the expression of Ly6g and S100a8. These markers are also expressed by Cd14+ inflammatory monocytes. I believe the authors need to additionally validate that these cells are neutrophils (via staining or additional analyses). Neutrophils are notoriously difficult to capture in scRNA-seq given low RNA content. Later, they are quantified by FACS using CD11b+Ly6G+ markers, but I do not believe this would distinguish them from CD14+ monocytes. As this is a relatively minor aspect of the manuscript, I consider this a minor concern, but a finding that should be as accurate as possible as Il1b is likely important, and identifying its accurate source likewise.

Thanks a lot for reviewer’s constructive comments. According to the reviewer’s suggestion, we have now added Cd14 expression in Figure 1C, and found that indeed cluster 27 express not only expressed Ly6G but also expressed Cd14. Based on literatures, the expression of Ly6G in circulating blood, spleen, and peripheral tissues is limited to neutrophils, whereas monocytes, macrophages, and lymphocytes are negative of Ly6G (Ikeda et al., 2023; Lee, Wang, Parisini, Dascher, & Nigrovic, 2013). Therefore, Ly6G can be used as a marker to distinguish neutrophils and monocytes. Although CD14 is highly expressed in monocytes, neutrophils can also express CD14 at lower level (Antal-Szalmas, Strijp, Weersink, Verhoef, & Van Kessel, 1997). Therefore, the cluster 27 is likely a mixed population of neutrophils and monocytes. So we have changed the definition of this cluster as NEU/Mon in the updated manuscript.

To confirm the presence of neutrophils and monocytes in ACD, we have included new FACS analysis of inflammatory monocytes, which are gated as CD11B+Ly6G-F4/80-CD11C-Ly6Chi, according to published FACS protocol(Rose, Misharin, & Perlman, 2012). We found that elicitation of ACD led to a transient influx of monocytes at 24 hrs post treatment, whereas the percentage of neutrophils continued to increase by 60 hours post-treatment (Figure 3L, and Figure 3-figure supplement 1G). In addition, at 60 hrs, the percentage of neutrophils (~5%) was > 10 times greater than the percentage of monocytes (~0.4%), indicating that neutrophils are the dominant granulocytes at 60 hours post ACD elicitation.

(3) The authors should include a cluster marker table as a supplementary file to accompany Figure 1C. Only top cluster markers are shown in 1C.

Thanks a lot for reviewer’s constructive comments. We have now included the top 5 enriched genes in each cell clusters shown in Fig. 1C in supplementary Table S2.

(4) Figures 2A/B have mismatched labels. There is a gdT/ILC2 label in the 2B, but not in 2A. Please match these. Along these lines, which gdT cluster is the IL17A expressing cluster as shown in 1D? Matching these labels will clarify which population is doing what.

Thanks a lot for reviewer to point out this mistake. To avoid confusion about the T cell clusters, we have added a specific recluster# for the T cell clusters as r0~r7 (Figure 2A-B). The r4 cluster is a mixed population of δγT and ILC2, therefore termed as δγT/ILC2. As shown in Figure 2-figure supplement 1E, IL17A is primarily expressed in the δγT cell (r5). We have now corrected δγT2 to δγT/ILC2 throughout the manuscript. To avoid confusion, we have now added cluster # in updated Figure 2D.

(5) In Figure 3E, the authors used CD11B as a distinguishing marker for basophils (CD11B+) vs. mast cells (CD11B-). Mcpt8 is a better distinguishing marker, so I am wondering why the authors chose CD11B.

Thanks a lot for reviewer’s comments. In scRNAseq, we did use Mcpt8 as a basophil specific marker to distinguish basophils and mast cells (see Figure 1C). However, Mcpt8 is not a surface receptor that can be used in FACS analysis. Therefore, to distinguish basophils from mast cells by FACS, we have to choose surface markers expressed on these cells. FcεR1a is a highly specific markers expressed exclusively on basophils and mast cells, and CD11B is expressed on basophils but not in mature mast cells (Hamey et al., 2021). As a result, FACS analysis of the surface expression of CD11B and FceR1a can distinguish basophils (CD11B+ FcεR1a+) from mast cells (CD11B- FcεR1a+). The use of CD11B and FcεR1a to distinguish basophils and mast cells can also been see in a published reference study (Arinobu et al., 2005).

(6) Antibody information is missing for IF studies. No clones, catalog numbers, vendors, RRIDs, or dilutions are included in the Methods section for any of the IF data.

Thanks a lot for reviewer’s constructive comments. We have now added related information for all the antibodies we used for FACS or IF data in the method section.

(7) Figure 3 supplement E and F appear to be reversed based on legend descriptions.

Thank a lot for pointing this out. We have now made the correction in the updated Supplementary file.

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eLife assessment

This important study uses single-cell RNA-seq to obtain a more granular understanding of cell subsets within allergic contact dermatitis in a model system with DNFB. The convincing data revela unique subpopulations of dermal fibroblasts as key responders to interferon gamma and likely as mediators of dermatitis. This study has many novel aspects and provides a unique resource as well.

Reviewer #1 (Public Review):

In this manuscript, Liu et al. used scRNA-seq to characterize cell type-specific responses during allergic contact dermatitis (ACD) in a mouse model, specifically the hapten-induced DNFB model. Using the scRNA-seq data, they deconvolved the cell types responsible for the expression of major inflammatory cytokines such as IFNG (from CD4 and CD8 T cells), IL4/13 (from basophils), IL17A (from gd T cells), and IL1B from neutrophils and macrophages. They found the highest upregulation of a type 1 inflammatory response, centering around IFNG produced by CD4 and CD8 T cells. They further identified a subpopulation of dermal fibroblasts (pre-adipocytes found in the dermal white adipose tissue layer) that upregulate CXCL9/10 during ACD and provide functional genetic evidence in their mouse model that disrupting IFNG signaling in fibroblasts decreases CD8 T cell infiltration and overall inflammation. They identify an increase in IFNG-expressing CD8 T cells in human patient samples of ACD vs. healthy control skin and co-localization of CD8 T cells with PDGFRA+ fibroblasts, which suggests this mechanism is relevant to human ACD. This mechanism is reminiscent of recent work showing that IFNG signaling in dermal fibroblasts upregulates CXCL9/10 to recruit CD8 T cells in a mouse model of vitiligo. Overall, this is a well-presented, clear, and comprehensive manuscript. The conclusions of the study are well supported by the data, with thoughtful discussion on study limitations by the authors. One such limitation was the use of one ACD model (DNFB), which prevents an assessment of how broadly relevant this axis is. The human sample validation is limited by the multiplexing capacity of immunofluorescence markers but shows a predominance of CD8+/IFNG+ cells and PDGFRA+/CXCL10+ cells in ACD (which are virtually absent in healthy control), along with co-localization of CD8+ cells with PDGFRA+ cells. Thus, this mechanism is likely active in human ACD.

Strengths:<br /> Through deep characterization of the in vivo ACD model using scRNA-seq, the authors were able to determine which cell types were expressing the major cytokines involved in ACD inflammation, such as IFNG, IL4/13, IL17A, and IL1B. These analyses are well-presented and thoughtful, showing first that the response is IFNG-dominant, then focusing on deeper characterization of lymphocytes, myeloid cells, and fibroblasts, which are also validated and complemented by FACS experiments using canonical markers of these cell types as well as IF staining. Crosstalk analyses from the scRNA-seq data led the authors to focus on IFNG signaling fibroblasts, and in vitro experiments demonstrate that CXCL9 and CXCL10 are expressed by fibroblasts stimulated by IFNG. In vivo functional genetic evidence demonstrates an important role for IFNG signaling in fibroblasts, as KO of Ifngr1 using Pdgfra-Cre Ifngr1 fl/fl mice, showed a reduction in inflammation and CD8 T cell recruitment. Human ACD sample staining demonstrates the likely activity of the CD8 T cell IFNG-driven fibroblast response in human disease.

Weaknesses:<br /> The use of one model limits an understanding of how broad this fibroblast-T cell axis is during ACD. However, the authors chose the most commonly employed model and compared their data to work in a vitiligo model (another type 1 immune response) to demonstrate similar mechanisms at play. Human patient samples of ACD were co-stained with two markers at a time, demonstrating the presence of CD8+IFNG+ T cells, PDGFRA+CXCL10+ fibroblasts, and co-localization of PDGFRA+ fibroblasts and CD8+ T cells. However, no IF staining demonstrates co-expression of all 4 markers at once; thus, the human validation of co-localization of CD8+IFNG+ T cells and PDGFRA+CXCL10+ fibroblasts is ultimately indirect, although more likely than not to be true.

Reviewer #2 (Public Review):

Summary: The investigators apply scRNA seq and bioinformatics to identify biomarkers associated with the DNFB-induced contact dermatitis in mice. The bioinformatics component of the study appears reasonable and may provide new insights regarding TH1 driven immune reactions in ACD in mice. However, the IF data and images of tissue sections are not clear and should be improved to validate the model.

Strengths:<br /> The bioinformatics analysis.

Weaknesses:<br /> The IF data presented in 4H, 6H, 7E and 7F are not convincing and need to be correlated with routine staining on histology and different IF markers for PDGFR. Some of the IF staining data demonstrates a pattern inconsistent with its target.

Author response:

The following is the authors’ response to the original reviews.

Main points:

(1) We have added data for fructose in Fig. 1

(2) We have added sta1s1cs (red stars and NS) comparing Tp between fed and refed flies. 

(3) We have modified the figure for each point to the opened small circles.

(4) We have moved the data from Fig. S3 to Fig. 2 and 3.

(5) We have added the schema1c diagrams depic1ng behavioral assay in Fig. S1.

(6) We have added heatmaps for WT and Gr64f-Gal4>UAS-CsChrimson flies in Fig. S2.

(7) We have added Orco1 mutant data in Fig. S4.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This paper presents valuable findings that gustation and feeding state influence the preferred environmental temperature preference in flies. Interestingly, the authors showed that by refeeding starved animals with the non-nutritive sugar sucralose, they are able to tune their preference towards a higher temperature in addition to nutrient-dependent warm preference. The authors show that temperature-sensing and sweet-sensing gustatory neurons (SGNs) are involved in the former but not the latter. In addition, their data indicate that pep3dergic signals involved in internal state and clock genes are required for taste-dependent warm preference behavior.

The authors made an analogy of their results to the cephalic phase response (CPR) in mammals where the thought, sight, and taste of food prepare the animal for the consumption of food and nutrients. They further linked this behavior to core regulatory genes and peptides controlling hunger and sleep in flies having homologues in mammals. These valuable behavioral results can be further inves3gated in flies with the advantage of being able to dissect the neural circuitry underlying CPR and nutrient homeostasis.

Strengths: 

(1) The authors convincingly showed that tasting is sufficient to drive warm temperature preference behavior in starved flies and that it is independent of nutrient-driven warm preference. 

(2) By using the genetic manipulation of key internal sensors and genes controlling internal feeding and sleep states such as DH44 neurons and the per genes for example, the authors linked gustation and temperature preference behavior control to the internal state of the animal. 

Weaknesses: 

(1) The title is somewhat misleading, as the term homeostatic temperature control linked to gustation only applies to starved flies. 

We agree with the reviewer's suggestion and have changed the title to "Taste triggers a homeostatic temperature control in hungry flies".

(2) The authors used a temperature preference assay and refeeding for 5 minutes, 10 minutes, and 1 hour.

Experimentally, it makes a difference if the flies are tested immediately after 10 minutes or at the same 3me point as flies allowed to feed for 1 hour. Is 10 minutes enough to change the internal state in a nutrition-dependent manner? Some of the authors' data hint at it (e.g. refeeding with fly food for 10 minutes), but it might be relevant to feed for 5/10 minutes and wait for 55/50min to do the assays at comparable time points. 

Thank you for your suggestions. The temperature preference behavioral test itself takes 30 minutes from the time the flies are placed in the apparatus until the final choice is made. This means that after the hungry flies have been refed for 5 minutes, they will determine their preferred temperature within 35 minutes. It has been shown that insulin levels peak at 10 minutes and gradually decline (Tsao, et al., PLoS Genetics 2023). However, it is unclear how subtle insulin levels affect behavior and how quickly the flies are able to consume food. These factors may contribute to temperature preference in flies. Therefore, to minimize "extraneous" effects, we decided to test the behavioral assay immediately after they had eaten the food. We have noted in the material and method section that why we chose the condition based on behavior duration and insulin effect. 

(3) A figure depicting the temperature preference assay in Figure 1 would help illustrate the experimental approach. It is also not clear why Figure 1E is shown instead of full statistics on the individual panels shown above (the data is the same). 

We have revised Figure 1A and added statistics in Figure 1BCD. We also added a figure depicting the temperature preference assay (Fig. S1).

(4) The authors state that feeding rate and amount were not changed with sucralose and glucose. However, the FLIC assay they employed does not measure consumption, so this statement is not correct, and it is unclear if the intake of sucralose and glucose is indeed comparable. This limits some of the conclusions. 

We agree and removed “amount” and have revised the MS. 

(5) The authors make a distinction between taste-induced and nutrient-induced warm preference. Yet the statistics in most figures only show the significance between the starved and refed flies, not the fed controls. As the recovery is in many cases incomplete and used as a distinction of nutritive vs nonnutritive signals (see Figure 1E) it will be important to also show these additional statistics to allow conclusions about how complete the recovery is. 

We agree with the comments and have revised the MS and figures. 

(6) The starvation period used is ranging from 1 to 3 days, as in some cases no effect was seen upon 1 day of starvation (e.g. with clock genes or temperature sensing neurons). While the authors do provide a comparison between 18-21 and 26-29 hours old flies in Figure S1, a comparison for 42-49 and 66-69 hours of starvation is missing. This also limits the conclusion as the "state" of the animal is likely quite different after 1 day vs. 3 days of starvation and, as stated by the authors, many flies die under these conditions.  

We mainly used 2 overnights of starvation.  Some flies (e.g. Ilp6 mutants) were completely healthy even after 2 overnights of starvation, we had to starve them for 3 overnights. For example, Ilp6 mutants needed 3 overnights of starvation to show a significant difference Tp between fed and starved flies. On the other hand, some flies (e.g. w1118 control flies) were very sick after 2 overnights of starvation, we had to starve them for one overnight. Therefore, the starvation conditions which we used for this manuscript are from 1- 3-overnights.

First, we confirmed the starvation time by focusing on Tp which resulted in a sta1s1cally significant Tp difference between fed and starved flies; as men1oned above, flies prefer lower temperatures when starvation is prolonged (Umezaki et al., Current Biology 2018). Therefore, if Tp was not statistically different between fed and starved flies, we extended the starva1on 1me from 1 to 3 overnights. Importantly, we show in Fig. S3 that the dura1on of starvation did not affect the recovery effect. Furthermore, since control flies do not survive 42-49 or 66-69 hours of starvation, we can not test the reviewer's suggestion. We have carefully documented the conditions in the Material and method and figure legends.

(7) In Figure 2, glucose-induced refeeding was not tested in Gr mutants or silenced animals, which would hint at post-ingestive recovery mechanisms related to nutritional intake. This is only shown later (in Figure S3) but I think it would be more fitting to address this point here. The data presented in Figure S3 regarding the taste-evoked vs nutrient-dependent warm preference is quite important while in some parts preliminary. It would nonetheless be justified to put this data in the main figures. However, some of the conclusions here are not fully supported, in part due to different and low n numbers, which due to the inherent variability of the behavior do not allow statistically sound conclusions. The authors claim that sweet GRNs are only involved in taste-induced warm preference, however, glucose is also nutritive but, in several cases, does not rescue warm preference at all upon removal of GRN function (see Figures S3A-C). This indicates that the Gal4 lines and also the involved GRs are potentially expressed in tissues/neurons required for internal nutrient sensing. 

Thank you for your suggestion. We have added Figure S3ABC (glucose refeeding using Gr mutants and silenced animals) to Figure 2. There is no low N number since we tested > 5 times, i.e. >100 flies were tested. Tp may have a variation probably due to the effect of starvation on their temperature preference. 

We did not mention that "The authors claim that sweet GRNs are only involved in taste-induced warm preference...". However, our wri1ng may not be clear enough. We agree that "...GRs may be expressed in tissues/neurons required for internal nutrient sensing. ..."  We have rewritten and revised the section.  

(8) In Figure 4, fly food and glucose refeeding do not fully recover temperature preference after refeeding. With the statistical comparison to the fed control missing, this result is not consistent with the statement made in line 252. I feel this is an important point to distinguish between state-dependent and taste/nutrition-dependent changes.  

We inserted the statistics and compared between Fed and other conditions. 

(9) The conclusion that clock genes are required for taste-evoked warm preference is limited by the observation that they ingest less sucralose. In addition, the FLIC assay does not allow conclusions about the feeding amount, only the number of food interactions. Therefore, I think these results do not allow clear-cut conclusions about the impact of clock genes in this assay.  

We agree and remove “amount” and have revised the MS. The per01 mutants ate (touched) sucralose more often than glucose. On the other hand, 1m01 mutants ate glucose more often than sucralose (Figure S6BC). However, these mutants s1ll showed a similar TP pattern for sucralose and glucose refeeding (Fig. 5CD). The results suggest that the 1m01 flies eat enough amount of sucralose over glucose that their food intake does not affect the TP behavioral phenotype. We have rewritten and revised the section.

(10) CPR is known to be influenced by taste, thought, smell, and sight of food. As the discussion focused extensively on the CPR link to flies it would be interesting to find out whether the smell and sight of food also influence temperature preference behavior in animals with different feeding states.  

We have added the data using Olfactory receptor co-receptor (Orco1) mutant, which lack olfaction, in Fig. S4. They failed to show the taste-evoked warm preference, but exhibited the nutrient-induced warm preference. Therefore, the data suggest that olfactory detection is also involved in taste-evoked warm preference. On the other hand, "seeing food" is probably more complicated, since light dramatically affects temperature preference behavior and the circadian clock that regulates temperature preference rhythms. Therefore, it will not be unlikely to draw a solid conclusion from the short set of experiments. We will address this issue in the next study.

(11) In the discussion in line 410ff the authors claim that "internal state is more likely to be associated with taste-evoked warm preference than nutrient-induced warm preference." This statement is not clear to me, as neuropeptides are involved in mediating internal state signals, both in the brain itself as well as from gut to brain. Thus, neuropeptidergic signals are also involved in nutrient-dependent state changes, the authors might just not have identified the peptides involved here. The global and developmental removal of these signals also limits the conclusions that can be drawn from the experiments, as many of these signals affect different states, circuits, and developmental progression.  

We agree with the comments. We have removed the sentences and revised the MS.  

Reviewer #2 (Public Review): 

Animals constantly adjust their behavior and physiology based on internal states. Hungry animals, desperate for food, exhibit physiological changes immediately upon sensing, smelling, or chewing food, known as the cephalic phase response (CPR), involving processes like increased saliva and gastrointestinal secretions. While starvation lowers body temperature, the mechanisms underlying how the sensation of food without nutrients induces behavioral responses remain unclear. Hunger stress induces changes in both behavior and physiological responses, which in flies (or at least in Drosophila melanogaster) leads to a preference for lower temperatures, analogous to the hunger-driven lower body temperature observed in mammals. In this manuscript, the authors have used Drosophila melanogaster to investigate the issue of whether taste cues can robustly trigger behavioral recovery of temperature preference in starving animals. The authors find that food detection triggers a warm preference in flies. Starved flies recover their temperature preference after food intake, with a distinction between partial and full recovery based on the duration of refeeding. Sucralose, an artificial sweetener, induces a warm preference, suggesting the importance of food-sensing cues. The paper compares the effects of sucralose and glucose refeeding, indicating that both taste cues and nutrients contribute to temperature preference recovery. The authors show that sweet gustatory receptors (Grs) and sweet GRNs (Gustatory Receptor Neurons) play a crucial role in taste-evoked warm preference. Optogenetic experiments with CsChrimson support the idea that the excitation of sweet GRNs leads to a warm preference. The authors then examine the internal state's influence on taste-evoked warm preference, focusing on neuropeptide F (NPF) and small neuropeptide F (sNPF), analogous to mammalian neuropeptide Y. Mutations in NPF and sNPF result in a failure to exhibit taste-evoked warm preference, emphasizing their role in this process. However, these neuropeptides appear not to be critical for nutrient-induced warm preference, as indicated by increased temperature preference during glucose and fly food refeeding in mutant flies. The authors also explore the role of hunger-related factors in regula3ng taste-evoked warm preference. Hunger signals, including diuretic hormone (DH44) and adipokinetic hormone (AKH) neurons, are found to be essential for taste-evoked warm preference but not for nutrient-induced warm preference. Additionally, insulin-like peptides 6 (Ilp6) and Unpaired3 (Upd3), related to nutritional stress, are identified as crucial for taste-evoked warm preference. The investigation then extends into circadian rhythms, revealing that taste-evoked warm preference does not align with the feeding rhythm. While flies exhibit a rhythmic feeding pattern, taste-evoked warm preference occurs consistently, suggesting a lack of parallel coordination. Clock genes, crucial for circadian rhythms, are found to be necessary for taste-evoked warm preference but not for nutrient-induced warm preference. 

Strengths: 

A well-written and interesting study, investigating an intriguing issue. The claims, none of which to the best of my knowledge controversial, are backed by a substantial number of experiments. 

Weakness: 

The experimental setup used and the procedures for assessing the temperature preferences of flies are rather sparingly described. Additional details and data presentation would enhance the clarity and replicability of the study. I kindly request the authors to consider the following points: 

i) A schematic drawing or diagram illustrating the experimental setup for the temperature preference assay would greatly aid readers in understanding the spatial arrangement of the apparatus, temperature points, and the positioning of flies during the assay. The drawing should also be accompanied by specific details about the setup (dimensions, material, etc). 

Thank you for your suggestions. We have added the schematic drawing in Fig. S1.

ii) It would be beneficial to include a visual representation of the distribution of flies within the temperature gradient on the apparatus. A graphical representation, such as a heatmaps or histograms, showing the percentage of flies within each one-degree temperature bin, would offer insights into the preferences and behaviors of the flies during the assay. In addition to the detailed description of the assay and data analysis, the inclusion of actual data plots, especially for key findings or representative trials, would provide readers with a more direct visualization of the experimental outcomes. These additions will not only enhance the clarity of the presented information but also provide the reader with a more comprehensive understanding of the experimental setup and results. I appreciate the authors' attention to these points and look forward to the potential inclusion of these elements in the revised manuscript. 

Thank you for the advice. We have added the heat map for WT and Gr64fGal4>CsChrimson data in Fig. S2. 

Reviewer #3 (Public Review): 

Summary: 

The manuscript by Yujiro Umezaki and colleagues aims to describe how taste stimuli influence temperature preference in Drosophila. Under starvation flies display a strong preference for cooler temperatures than under fed conditions that can be reversed by refeeding, demonstrating the strong impact of metabolism on temperature preference. In their present study, Umezaki and colleagues observed that such changes in temperature preference are not solely triggered by the metabolic state of the animal but that gustatory circuits and peptidergic signalling play a pivotal role in gustation-evoked alteration in temperature preference. 

The study of Umezaki is definitively interesting and the findings in this manuscript will be of interest to a broad readership. 

Strengths: 

The authors demonstrate interesting new data on how taste input can influence temperature preference during starvation. They propose how gustatory pathways may work together with thermosensitive neurons, peptidergic neurons and finally try to bridge the gap between these neurons and clock genes. The study is very interesting and the data for each experiment alone are very convincing. 

Weaknesses: 

In my opinion, the authors have opened many new questions but did not fully answer the initial question - how do taste-sensing neurons influence temperature preferences? What are the mechanisms underlying this observation? Instead of jumping from gustatory neurons to thermosensitive neurons to peptidergic neurons to clock genes, the authors should have stayed within the one question they were asking at the beginning. How does sugar sensing influence the physiology of thermos-sensation in order to change temperature preference? Before addressing all the following question of the manuscript the authors should first directly decipher the neuronal interplay between these two types of neurons. 

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Figure S3D is cited before S2, so please rearrange the numbering.

Thank you. We have changed the numbering.

I would also suggest a different color to visualize the data points in Figure S3, as some are barely visible on the dark bars (e.g. on a dark green background). 

We have revised the figures. The data points were changed to smaller opened circles. 

Reviewer #2 (Recommendations For The Authors): 

*Please, expand on the experimental procedure, and describe the assay in detail. 

We have added a scheme for the assay in Fig. S1 and also have revised the manuscript and figures.

*Show the distribution of the gradient data that the preference values are based upon. Not necessarily for all, but for select key experiments. Heatmaps for each replicate (stacked on top of each other) would be a nice way of showing this. Simple histograms would of course work as well. 

We have added heatmaps of selected key experiments that were added in Fig. S2. We have revised the manuscript and figures, correspondingly.

Reviewer #3 (Recommendations For The Authors  

The manuscript by Yujiro Umezaki and colleagues aims at describing how taste stimuli influence temperature preference in Drosophila. Under starvation, flies display a strong preference for cooler temperatures than under-fed conditions that can be reversed by refeeding, demonstrating the strong impact of metabolism on temperature preference. In their present study, Umezaki and colleagues observed that such changes in temperature preference are not solely triggered by the metabolic state of the animal but that gustatory circuits play a pivotal role in temperature preference. The study of Umezaki is definitively interesting and the findings in this manuscript will be of interest to a broad readership. However, I would like to draw the authors' attention to some points of concern: 

The title to me sounds somehow inadequate. The definition of homeostasis (Cambridge Dictionary) is as follows: "the ability or tendency of a living organism, cell, or group to keep the conditions INSIDE it the same despite any changes in the conditions around it, or this state of internal balance". What do the authors mean by homeostatic temperature control? Reading the title not knowing much about poikilotherm insects I would understand that the authors claim that Drosophila can indeed keep a temperature homeostasis as mammals do. As Drosophila is not a homoiotherm animal and thus cannot keep its body temperature stable the title should be amended.  

Homeostasis means a state of balance between all the body systems necessary for the body to survive and function properly. Drosophila are ectotherms, so the source of temperature comes from the environment, and their body temperature is very similar to that of their environment. However, the flies' temperature regulation is not simply a passive response to temperature. Instead, they actively seek a temperature based on their internal state. We have shown that the preferred temperature increases during the day and decreases during the night, showing a circadian rhythm of temperature preference (TPR). Because their environmental temperature is very close to their body temperature, TPR gives rise to body temperature rhythms (BTR). We have shown that TPR is similar to BTR in mammals. (Kaneko et al., Current Biology 2012 and Goda et al., JBR 2023). Similarly, we showed that the hungry flies choose a lower temperature so that the body temperature is also lower. Therefore, our data suggest that the fly maintains its homeostasis by using the environmental temperature to adjust its body temperature to an appropriate temperature depending on its internal state. Therefore, I would like to keep the title as "Taste triggers a homeostatic temperature control in hungry flies" We have added more explana1on in the Introduc1on and Discussion.

Accordingly, the authors compare the preference of flies to cooler temperatures to the reduced body temperature of mammals (Lines 64 - 65). However, according to the cited literature the reduced body temperature in starved rats is discussed to reduce metabolic heat production (Sakurada et al., 2000). The authors should more rigorously give a short summary of the findings in the cited papers and the original interpretation to help the reader not get confused.

In flies, it has been shown that a lower temperature means a lower metabolic rate, and a higher temperature means a higher metabolic rate. Therefore, hungry flies choose a lower temperature where their metabolic rate is lower and they do not need as much heat.

Similarly, in mammals, starvation causes a lower body temperature, hypothermia. Body temperature is controlled by the balance between heat loss and heat production. The starved mammals showed lower heat production. We have added this information to the introduction. 

The authors show that 5 min fly food refeeding causes a par3al recovery of the naïve temperature preference of the flies (Figure 1B) and that feeding of sucralose par3ally rescues the preference whereas glucose rescues the preference similar to refeeding with fly food would do. As glucose is both sweet and metabolically valuable it would be clearer for the reader if the authors start with the fly food experiment and then show the glucose experiment to show that the altered temperature preference depends on the food component glucose. From there they can further argue that glucose is both sweet (hedonic value) and metabolically valuable. And to disentangle sweetness from metabolism one needs a sugar that is sweet but cannot be metabolized - sucralose. 

Thank you for your advice. Since the data with sucralose is the one we want to highlight the most, we decided to present it in the order of sucralose, glucose, and fly food.

In the sucralose experiment the authors omit the 5 min data point and only show the 10 min time point. As Figure 1F indicates that both Glucose and Sucralose elicit the same attractiveness in the flies and that sweetness influences the temperature preference, it is important that the authors show the 5 min temperature preference too to underline the effect of the sweet taste stimulus on the fly behavior independent from the caloric value. Further, the authors should demonstrate not only the cumulative touches but how much sucralose or glucose may already be consumed by the fly in the depicted time frames. 

It is interesting to see how much sucralose or glucose the flies consume over the time frames shown. Although the cumula1ve exposure to sugar is ideally equivalent to the amount of sugar, we need a different way to actually measure the amount of sugar. We will now emphasize "cumulative touches" rather than "amount of sugar" in the text. In the next study, we will look at how much sucralose or glucose the fly has already consumed.

Sucralose and Glucose have a similar molecular structure - it would be interesting to see how the sweet taste of a sugar with a different molecular structure like fructose and its receptor Gr43b (Myamato & Amrein 2014) may contribute to temperature preferences.  

Sucralose and Glucose are not structurally similar. That said, we tested fructose refeeding anyway. The hungry flies showed a taste-evoked warm preference after fructose refeeding. We have added data in Figure 1E and F. The data suggest that sweet taste is more important than sugar structure. We also tested Gr43b>CsChrimson. However, the flies do not show the taste-evoked warm preference (data not shown). The data suggest that Gr43b is not the major receptor controlling taste-evoked warm preference. We have revised the manuscript.

Both sugars appear similarly attractive to the flies (Figure 1F) - are water, sucralose, and glucose presented in a choice assay or are these individually in separate experiments? 

Water, sucralose, and glucose were individually presented in separate experiments. We clarified it in the figure legend.

Subsequently, the authors address the question of how sweet taste may influence temperature preferences in flies. To this end, the authors first employ gustatory receptor mutants for Gr5a, Gr64a, and Gr61a and demonstrate that sucralose feeding does not rescue temperature preference in the absence of sweet taste receptors. In an alternative approach, the authors do not use mutants but an expression of UAS:Kir in Gr64F neurons. Taking a closer look at the graph it appears that the Kir expressing flies have an increased (nearly 1{degree sign}C) temperature preference than the starved mutant flies. Is this preference change related to the mutation directly and what would be the result if Kir would be conditionally only expressed after development is completed, or is the observed temperature preference related to the Gr64f-Gal4 line? If the latter would be the case perhaps the authors may want to bring the flies to the same genetic background to allow for a more direct comparison of the temperature preferences. 

The Gr64fGal4>Kir flies show a ~one degree higher preferred temperature under starvation compared to the mutants. However, the phenotype is similar to the controls, Gr64fGal4/+ flies, under starvation. Therefore, this phenotype is not due to either the mutation or the Kir effect. Most importantly, the Gr64fGal4>Kir flies failed to show a taste-evoked warm preference. Together with other mutant data, we concluded that sweet GRNs are required for taste-evoked warm preference.

Overall, the figure legend for Figure 2 is very cryptic and should be more detailed.

We have revised the figure legend for Figure 2. 

To shed light on the mechanisms underlying the changes in temperature preferences through gustatory stimuli the authors next blocked heat and cold sensing neurons in fed and starved flies and found out that TrpA1 expressing anterior cells and R11F02-Gal4 expressing neurons both participate in sweetness-induced alteration of temperature preference in starved animals. At this point, it should be explicitly indicated in the figure that the flies need more than one overnight starva3on to display the behavior (Figure 3A). 

We have revised the manuscript.

The data provided by the authors indicate a kind of push-and-pull mechanism between heat and cold-sensing neurons under starvation that is somehow influenced by sweet taste sensing. Further, the authors demonstrate that TrpA1-as well as R11F02-Gal4 driven Chrimson activation is sufficient to partially rescue temperature preference under starvation. At this point is unclear why the authors use a tubGal80ts expression system but not for the TrpA1SH-Gal4 driven Chrimson. As the development itself and the conditions under which the animals were raised may have influence on the temperature preference it is important that both groups are equally raised if the authors want to directly compare with each other. 

As we wrote in the Material and Method, the R11F02-Gal4>uas-CsChrimson flies died during the development. Therefore, we had to use tubGal80ts. On the other hand, the TrpA1-Gal4>CsChrimson flies can survive to adults. As we mentioned in MS, all flies were treated with ATR after they had fully developed into adults. This means that both TrpA1-Gal4 and R11F02-Gal4 expressing cells are ac1vated by red light via CsChrimson only in adult stages. We carefully revised the MS.

It is a pity that the authors at this point have decided to not deepen the understanding of the circuitry between thermo-sensation and metabolic homeostasis but subsequently change the focus of their study to investigate how internal state influences taste-evoked warm preference in hungry flies. Using mutants for NPF and sNPF the authors demonstrate that both peptides play a pivotal role in taste-evoked warm preference after sucrose feeding but not for nutrient-induced warm preference. Similarly, they found that DH44, AKH and dILP6, Upd2 and Upd3 neurons are also required for taste-evoked warm preference but not for nutrient-induced warm preference. Here again, the authors do not keep the systems stable and change between inhibition of neurons through Kir and mutants for peptides. For a better comparison, it would be preferable to use always exactly the same technique to inhibit neuron signalling.

It would be interesting to find the neural circuity of thermo-sensation and metabolic homeostasis, but we do not have any luck so far. We will continue to look into the neural circuits which control taste-evoked warm preference and nutrient-induced warm preference. Since UAS-Kir is such a strong reporter, it may kill the flies sometime. So we couldn't use UAS-Kir for all Gal4 flies. 

DH44 is expressed in the brain and in the abdominal ganglion where they share the expression pattern with 4 Lk neurons per hemisphere. Seeing the impact of Lk signalling in metabolism (AlAnzi et al., 2010) the authors should provide evidence that the observed effect is indeed because of DH44 and not Lk.

It would be interesting to see if Lk may play a role in taste-evoked warm preference and/or nutrient-induced warm preference. We would like to systematically screen which neuropeptides and receptors are involved in the behavior in the next study. 

Seeing the results on dILP6 it is interesting that Li and Gong (2015) could show in larvae that cold-sensing neurons directly interact with dILP neurons in the brain. It would be interesting to see whether similar circuitry may exist in adult flies to regulate temperature preferences and these peptidergic neurons. Further, it appears interesting that again these animals need much longer time to display the observed shift in temperature (which again should be clearly indicated in the figure legend too). These observations should be more carefully considered in the discussion part too.

We have revised the manuscript.

In the last part of the study, the authors investigate how sensory input from temperature-sensitive cells may transmit information to central clock neurons and how these in turn may influence temperature preference under starvation. The experiments assume that DH44-expressing neurons play a role in the output pathway of the central clock. Using the clock gene null mutants per and tim the authors show that even though the animals display a significant starvation response neither per nor tim mutants exhibited taste-evoked warm preference, indicating a taste but not nutrient-evoked temperature preference regulation. 

The authors demonstrate interesting new data on how taste input can influence temperature preference during starvation. They propose how gustatory pathways may work together with thermosensitive neurons, peptidergic neurons and finally try to bridge the gap between these neurons and clock genes. The study is very interesting and the data for each experiment alone are very convincing. However, in my opinion, the authors have opened many new questions but did not fully answer the initial question - how do taste-sensing neurons influence temperature preferences? What are the mechanisms underlying this observation? Instead of jumping from gustatory neurons to thermosensitive neurons to peptidergic neurons to clock genes, the authors should have stayed within the one question they were asking at the beginning. How does sugar sensing influence the physiology of thermos-sensation? Before addressing all the following questions of the manuscript the authors should first directly decipher the neuronal interplay between these two types of neurons. 

Thank you for your suggestion. It would be interesting to find the neural circuity of thermo-sensation and metabolic homeostasis. We have tried but there is no luck so far. 

The authors could e.g., employ Ca or cAMP-imaging in anterior or cold-sensitive cells and see how the responsiveness of these cells may be altered after sugar feeding. Or at least follow the idea of Li and Gong about the thermos-regulation of dILP-expressing neurons. 

Thank you for your suggestion. Since we do not know how dlLP-expression neurons are involved in temperature response in the adult flies. We will focus on the cells using Calcium imaging for the next study.

Anatomical analysis using the GRASP technique may further help to understand the interplay of these neurons and give new insights into the circuitry underlying food preference alteration under starvation. 

Thank you for your suggestion. It would be interesting to find the neural circuity of thermo-sensation and metabolic homeostasis. We have tried but there is no luck so far.  

Minor comments: 

Line 51: Hungry animals are desperate for food - I think the authors should not anthropomorphize at this point too\ much but rather strictly describe how the animals change their behavior without any interpretation of the mental state of the animal. 

We have modified the manuscript.

Line 80: Hunger and satiety dramatically affect animal behavior and physiology and control feeding - please not only cite the papers but also give a short overview of the cited papers on which behaviors are altered and how. 

We have revised the manuscript. 

Overall statistic: The authors do comparative statistics always against starved animals throughout but often state in the text a comparison against fed (Line 111: "but did not reach that of the fed flies") I think the authors should describe the date according to their statistics and keep this constant throughout the paper. 

Sorry for the confusion. We originally had it, but we removed it. We have added the additional statistical analyses.  

Figure legends: Overall the figure legends could be more developed and more detailed.

We have revised the manuscript.

eLife assessment

This paper presents valuable findings that gustation and nutrition might independently influence the preferred environmental temperature in flies. The evidence supporting the main claims is solid and well presented. The finding that flies might thus exhibit a cephalic phase response similar to mammals will be of value for future investigations.

Reviewer #1 (Public Review):

Summary:

This paper presents valuable findings that gustation and feeding state influence the preferred environmental temperature preference in flies. Interestingly, the authors showed that by refeeding starved animals with non-nutritive sugar sucralose, they are able to tune their preference towards a higher temperature in addition to nutrient-dependent warm preference. The authors show that temperature sensing and sweet sensing gustatory neurons (SGNs) are involved in the former but not the latter. In addition, their data indicate that peptidergic signals involved in internal state and clock genes are required for taste-dependent warm preference behavior.

The authors made an analogy of their results to the cephalic phase response (CPR) in mammals where the thought, sight and taste of food prepares the animal for the consumption of food and nutrients. The authors showed that taste triggers CPR-induced temperature preference behaviors in flies. The authors also briefly covered that the combined modalities of smell and taste induced CPR responses, showing that starved orco mutant flies failed to recover temperature preference after refeeding with sucralose.

The findings of this work hold promising future research prospects, for example, whether the sight of food influences temperature preference behavior in hungry flies, or whether taste, smell and sight work together or independently in promoting CPR responses.

Futhermore, these valuable behavioral results can be further investigated in flies with the advantage of being able to dissect the neural circuitry underlying CPR and nutrient homeostasis.

Strengths:

(1) The authors convincingly showed that tasting is sufficient to drive warm temperature preference behavior in starved flies and show that it is independent of nutrient-driven warm preference.<br /> (2) By using the genetic manipulation of key internal sensors and genes controlling internal feeding and sleep state such as DH44 neurons and the per genes for eg the authors linked gustation and temperature preference behavior control to the internal state of the animal.

Weaknesses:

Most of the weaknesses of the paper have been addressed in the revision. The points mentioned below are meant to improve readability of the paper and to promote understanding of the significance of the work.<br /> (1) Supplementary fig 1 could replace Figure 1A. The purpose of Figure 1F is not clear to me as the comparison between the different food substances is not separately addressed anywhere in the text.<br /> (2) The data for the orco receptor mutant could be placed in the main figures to justify the discussion emphasising CPR-like responses.

Reviewer #2 (Public Review):

Animals constantly adjust behavior and physiology based on internal states. Hungry animals, desperate for food, exhibit physiological changes immediately upon sensing, smelling, or chewing food, known as the cephalic phase response (CPR), involving processes like increased saliva and gastrointestinal secretions. While starvation lowers body temperature, the mechanisms underlying how the sensation of food without nutrients induces behavioral responses remain unclear. Hunger stress induces changes in both behavior and physiological responses, which in flies (or at least in Drosophila melanogaster) leads to a preference for lower temperatures, analogous to the hunger-driven lower body temperature observed in mammals. In this manuscript, the authors have used Drosophila melanogaster to investigate the issue of whether taste cues can robustly trigger behavioral recovery of temperature preference in starving animals. The authors find that food detection triggers a warm preference in flies. Starved flies recover their temperature preference after food intake, with a distinction between partial and full recovery based on the duration of refeeding. Sucralose, an artificial sweetener, induces a warm preference, suggesting the importance of food-sensing cues. The paper compares the effects of sucralose and glucose refeeding, indicating that both taste cues and nutrients contribute to temperature preference recovery. The authors show that that sweet gustatory receptors (Grs) and sweet GRNs (Gustatory Receptor Neurons) play a crucial role in taste-evoked warm preference. Optogenetic experiments with CsChrimson support the idea that the excitation of sweet GRNs leads to a warm preference. The authors then examine the internal state's influence on taste-evoked warm preference, focusing on neuropeptide F (NPF) and small neuropeptide F (sNPF), analogous to mammalian neuropeptide Y. Mutations in NPF and sNPF result in a failure to exhibit taste-evoked warm preference, emphasizing their role in this process. However, these neuropeptides appear not to be critical for nutrient-induced warm preference, as indicated by increased temperature preference during glucose and fly food refeeding in mutant flies. The authors also explore the role of hunger-related factors in regulating taste-evoked warm preference. Hunger signals, including diuretic hormone (DH44) and adipokinetic hormone (AKH) neurons, are found to be essential for taste-evoked warm preference but not for nutrient-induced warm preference. Additionally, insulin-like peptide 6 (Ilp6) and Unpaired3 (Upd3), related to nutritional stress, are identified as crucial for taste-evoked warm preference. The investigation then extends into circadian rhythms, revealing that taste-evoked warm preference does not align with the feeding rhythm. While flies exhibit a rhythmic feeding pattern, taste-evoked warm preference occurs consistently, suggesting a lack of parallel coordination. Clock genes, crucial for circadian rhythms, are found to be necessary for taste-evoked warm preference but not for nutrient-induced warm preference.

Strengths:

A well-written and interesting study, investigating an intriguing issue. The claims, none of which to the best of my knowledge controversial, are backed by a substantial number of experiments.

Weakness:

The experimental setup used and the procedures for assessing the temperature preferences of flies is rather sparingly described. Additional details and data presentation would enhance the clarity and replicability of the study. I kindly request the authors to consider the following points: i) A schematic drawing or diagram illustrating the experimental setup for the temperature preference assay would greatly aid readers in understanding the spatial arrangement of the apparatus, temperature points, and the positioning of flies during the assay. The drawing should also be accompanied by specific details about the setup (dimensions, material, etc). ii) It would be beneficial to include a visual representation of the distribution of flies within the temperature gradient on the apparatus. A graphical representation, such as a heatmaps or histograms, showing the percentage of flies within each one-degree temperature bin, would offer insights into the preferences and behaviors of the flies during the assay. In addition to the detailed description of the assay and data analysis, the inclusion of actual data plots, especially for key findings or representative trials, would provide readers with a more direct visualization of the experimental outcomes. These additions will not only enhance the clarity of the presented information but also provide the reader with a more comprehensive understanding of the experimental setup and results. I appreciate the authors' attention to these points and look forward to the potential inclusion of these elements in the revised manuscript.

Update: The revised manuscript now includes heatmaps showing the distribution of the flies across the temperature bins. As well as a schematic drawing of the behavioral setup.

eLife assessment

In this manuscript, Jain and colleagues explore whether increasing adult-born neurons is protective against status epilepticus and the development of spontaneous recurrent seizures (chronic epilepsy) in a mouse pilocarpine model of temporal lobe epilepsy. This is an important work that provides solid data, contradicting previous studies on suppressing chronic seizures by reduction in adult-born neurons.

Reviewer #1 (Public Review):

Summary:

As adult-born granule neurons have been shown to play diverse roles, both positive and negative, to modulate hippocampal circuitry and function in epilepsy, understanding the mechanisms by which altered neurogenesis contribute to seizures is important for future therapeutic strategies. The work by Jain et al., demonstrates that increasing adult-born neurons (not increasing adult neurogenesis because BrdU birthdating was not performed in this study) before status epilepticus (SE) leads to a suppression in chronic seizures in the pilocarpine model of temporal lobe epilepsy. This work is potentially interesting because previous studies showed suppressing adult-born neurons led to reduced chronic seizures.

To increase adult-born neurons, the authors conditionally delete the pro-apoptotic gene Bax using a tamoxifen inducible Nestin-CreERT2 which has been previously published to increase proliferation and survival of adult-born neurons by Sahay et al. (although this was not shown in this study). After 6 weeks of tamoxifen injection, the authors subject male and female mice to pilocarpine induced SE. In the first study, at 2 hours after pilocarpine, the authors examine latency to the first seizure, severity and total number of acute seizures, and power during SE. In the second study in a separate group of mice, the authors examine chronic seizure number and frequency, seizure duration, postictal depression, and seizure distribution/cluster seizures for 3 weeks after pilocarpine. Overall, the study concludes that increasing adult-born neurons in the normal adult brain can reduce epilepsy in females specifically.

Strengths:

(1) The study is sex matched and reveals differences in response to increasing adult-born neurons in chronic seizures between male and females.

(2) The EEG recording parameters are stringent, and analysis of chronic seizures is comprehensive. In two separate experiments, the electrodes were implanted to record EEG from cortex as well as hippocampus. The recording is done for 10 hours post pilocarpine to analyze acute seizures, and for 3 weeks continuous video EEG recording was done to analyze chronic seizures.

Weaknesses:

(1) Increased DCX alone (without birthdating with BrdU) could indicate increased survival of adult-born neurons, not proliferation or birth of newborn neurons per se. While prior work has demonstrated that tamoxifen injection in adult mice showed an increase in dentate gyrus neurogenesis based on studies of BrdU, Ki67, and DCX (Sahay et al., 2011), the dynamics of adult-born neurons (proliferation, differentiation, and/or survival) could be different in epileptic (pilocarpine-treated) animals. Other stages, e.g., proliferation of neural precursors or maturation of adult-born dentate granule cells, was not examined. Analysis of additional stages of adult neurogenesis may reveal additional cellular understanding and add impact of the work on the field.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

As adult-born granule neurons have been shown to play diverse roles, both positive and negative, to modulate hippocampal circuitry and function in epilepsy, understanding the mechanisms by which altered neurogenesis contributes to seizures is important for future therapeutic strategies. The work by Jain et al. demonstrates that increasing adult neurogenesis before status epilepticus (SE) leads to a suppression of chronic seizures in the pilocarpine model of temporal lobe epilepsy. This work is potentially interesting because previous studies showed suppressing neurogenesis led to reduced chronic seizures.

To increase neurogenesis, the authors conditionally delete the pro-apoptotic gene Bax using a tamoxifen-inducible Nestin-CreERT2 which has been previously published to increase proliferation and survival of adult-born neurons by Sahay et al. After 6 weeks of tamoxifen injection, the authors subjected male and female mice to pilocarpine-induced SE. In the first study, at 2 hours after pilocarpine, the authors examine latency to the first seizure, severity and total number of acute seizures, and power during SE. In the second study in a separate group of mice, at 3 weeks after pilocarpine, the authors examine chronic seizure number and frequency, seizure duration, postictal depression, and seizure distribution/cluster seizures. Overall, the study concludes that increasing adult neurogenesis in the normal adult brain can reduce epilepsy in females specifically. However, important BrdU birthdating experiments in both male and female mice need to be included to support the conclusions made by the authors. Furthermore, speculative mechanisms lacking direct evidence reduce enthusiasm for the findings.

There are two suggestions. First, BrdU birthdating of newborn neurons is important to add to the paper so that there is support for the conclusions. Second, speculative text reduced enthusiasm. In response, we clarified the conclusions. We do not think that the clarified conclusions require BrdU birthdating (discussed further below). We also removed two schematics (and associated text) that we think the reviewer was referring to when speculation was mentioned.

We also want to point out something minor -that the times of injections listed above are not correct.

a. Seizures were not measured 2 hrs after pilocarpine; that is when the anticonvulsant diazepam was administered to males. 

b. Seizures were not measured 3 weeks after pilocarpine; the duration of recording was 3 weeks.  

(1) BrdU birthdating is required for conclusions.

We think that the Reviewer was suggesting birthdating because we were not clear about our conclusions, and we apologize for the confusion. The Reviewer stated that we concluded: “conditionally deleting Bax in Nestin-Cre+ cells leads to increased neurogenesis and hilar ectopic granule cells, thereby reducing chronic seizures.”  (Note this is a quote from the review).

However, we did not intend to conclude that. We intended to conclude that conditionally deleting Bax in Nestin-Cre+ mice reduced chronic seizures in the mouse model of epilepsy that we used. Also, that conclusion only pertained to females. Please note we did not conclude that hilar ectopic granule cells led to reduced seizures. We also concluded that Bax deletion increased neurogenesis in female mice. We have revised the text to make the conclusions clear.

Abstract, starting on line 67:

The results suggest that selective Bax deletion to increase adult neurogenesis can reduce experimental epilepsy, and the effect shows a striking sex difference.

Results, starting on line 448:

Because Cre+ epileptic females had increased numbers of immature neurons relative to Cre- females at the time of SE, and prior studies show that Cre+ females had less neuronal damage after SE (Jain et al., 2019), female Cre+ mice might have had reduced chronic seizures because of high numbers of immature neurons. However, the data do not prove a causal role.

Starting on line 477:

...we hypothesized that female Cre+ mice would have fewer hilar ectopic GCs than female Cre- mice. However, that female Cre+ mice did not have fewer hilar ectopic GCs.

Discussion, starting on line 563:

The chronic seizures, measured 4-7 weeks after pilocarpine, were reduced in frequency by about 50% in females. Therefore, increasing young adult-born neurons before the epileptogenic insult can protect against epilepsy. However, we do not know if the protective effect was due to the greater number of new neurons before SE or other effects. Past data would suggest that increased numbers of newborn neurons before SE leads to a reduced SE duration and less neuronal damage in the days after SE. That would be likely to lessen the epilepsy after SE. However, there may have been additional effects of larger numbers of newborn neurons prior to SE.

Conclusions, starting on line 745:

In the past, suppressing adult neurogenesis before SE was followed by fewer hilar ectopic GCs and reduced chronic seizures. Here, we show that the opposite - enhancing adult neurogenesis before SE and increased hilar ectopic GCs - do not necessarily reduce seizures. We suggest instead that protection of the hilar neurons from SE-induced excitotoxicity was critical to reducing seizures. The reason for the suggestion is that the survival of hilar neurons would lead to persistence of the normal inhibitory functions of hilar neurons, protecting against seizures. However, this is only a suggestion at the present time because we do not have data to prove it. Additionally, because protection was in females, sex differences are likely to have played an important role. Regardless, the results show that enhancing neurogenesis of young adult-born neurons in Nestin-Cre+ mice had a striking effect in the pilocarpine model, reducing chronic seizures in female mice.

The Reviewer is correct that it would be interesting to know when the increase in adult neurogenesis occurred that was critical to the effect. For example, was it the initial increase following Bax deletion but before pilocarpine-induced SE, or the increase in neurogenesis following SE, or increased adult neurogenesis in the chronic stage of epilepsy. It also might be that related aspects of neurogenesis played a role such as the degree that maturation was normal in adult-born neurons. We have not pursued the experiments to identify these aspects of neurogenesis because of how much work it would entail. Also, approaches to conclude cause-effect relationships are going to be difficult. 

(2) Speculation.

We removed the text and supplemental figures with schematics that we think were the overly speculative parts of the paper the Reviewer mentioned.

Strengths:

(1) The study is sex-matched and reveals differences in response to increasing adult neurogenesis in chronic seizures between males and females.

(2) The EEG recording parameters are stringent, and the analysis of chronic seizures is comprehensive. In two separate experiments, the electrodes were implanted to record EEG from the cortex as well as the hippocampus. The recording was done for 10 hours post pilocarpine to analyze acute seizures, and for 3 weeks continuous video EEG recording was done to analyze chronic seizures.

Weaknesses:

(1) Cells generated during acute seizures have different properties to cells generated in chronic seizures. In this study, the authors employ two bouts of neurogenesis stimuli (Bax deletion dependent and SE dependent), with two phases of epilepsy (acute and chronic). There are multiple confounding variables to effectively conclude that conditionally deleting Bax in Nestin-Cre+ cells leads to increased neurogenesis and hilar ectopic granule cells, thereby reducing chronic seizures.

As mentioned above, with a clarification of our conclusions we think we have addressed the concern. We believe that we conditionally deleted Bax in Nestin-expressing cells. We believe we found that female mice had reduced loss of hilar mossy cells and somatostatin-expressing neurons after SE, and fewer chronic seizures after SE. While it makes sense that increased neurogenesis caused the reduced seizures, we acknowledge it was not proved.

We do not make conclusions about the role of hilar ectopic granule cells. However, we note that they appear to have been similar in number across groups, which suggests they played no role in the results. This is very surprising and therefore adds novelty.

(2) Related to this is the degree of neurogenesis between Cre+ and Cre- mice and the nature of the sex differences. It is crucial to know the rate/fold change of increased neurogenesis before pilocarpine treatment and whether it is different between male and female mice.

We agree that if sex differences in adult neurogenesis could be shown by a sex difference in rate, fold change, maturation, and other characteristics.  However, sex differences can also be shown by a change in doublecortin (DCX), which is what we did. We respectfully submit that we do not see an exhaustive study is critical.

As a result, we have clarified DCX was studied either before SE or in the period of chronic seizures:

Results, starting on line 406:

III. Before and after epileptogenesis, Cre+ female mice exhibited more immature neurons than Cre- female mice but that was not true for male mice.

Starting on line 446:

Therefore, elevated DCX occurred after chronic seizures had developed in Cre+ mice but the effect was limited to females.

Discussion, starting on line 592:

This study showed that conditional deletion of Bax from Nestin-expressing progenitors increased young adult-born neurons in the DG when studied 6 weeks after deletion and using DCX as a marker of immature neurons.

(3) The authors observe more hilar Prox1 cells in Cre+ mice compared to Cre- mice. The authors should confirm the source of the hilar Prox1+ cells.

This is an excellent question but it is unclear that it is critical to the seizures since both sexes showed more hilar Prox1 cells in Cre+ mice but only the females had fewer seizures than Cre- mice. This is the additional text to describe the results (starting on Line 493):

In past studies, hilar ectopic GCs have been suggested to promote seizures (Scharfman et al., 2000; Jung et al., 2006; Cho et al., 2015). Therefore, we asked if the numbers of hilar ectopic GCs correlated with the numbers of chronic seizures. When Cre- and Cre+ mice were compared (both sexes pooled), there was a correlation with numbers of chronic seizures (Fig. 6D1) but it suggested that more hilar ectopic GCs improved rather than worsened seizures. However, the correlation was only in Cre- mice, and when sexes were separated there was no correlation (Fig. 6D3).

When seizure-free interval was examined with sexes pooled, there was a correlation for Cre+ mice (Fig. 6D2) but not Cre- mice. Strangely, the correlations of Cre+ mice with seizure-free interval (Fig. 6D2, D4) suggest ectopic GCs shorten the seizure-free interval and therefore worsen epilepsy, opposite of the correlative data for numbers of chronic seizures. In light of these inconsistent results it seems that hilar ectopic granule cells had no consistent effect on chronic seizures.

(4) The biggest weakness is the lack of mechanism. The authors postulate a hypothetical mechanism to reconcile how increasing and decreasing adult-born neurons in GCL and hilus and loss of hilar mossy and SOM cells would lead to opposite effects - more or fewer seizures. The authors suggest the reason could be due to rewiring or no rewiring of hilar ectopic GCs, respectively, but do not provide clear-cut evidence.

As we mention above, we removed the supplemental figures with schematics because they probably were what seemed overly speculative.

We acknowledge that mechanism is not proven by our study. However, we would like to mention that in our view, showing preservation of hilar mossy cells and SOM cells, but not PV cells, does add mechanistic data to the paper. We understand more experiments are necessary.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Jain et al explore whether increasing adult neurogenesis is protective against status epilepticus (SE) and the development of spontaneous recurrent seizures (chronic epilepsy) in a mouse pilocarpine model of TLE. The authors increase adult neurogenesis via conditional deletion of Bax, a pro-apoptotic gene, in Nestin-CreERT2Baxfl/fl mice. Cre- littermates are used as controls for comparisons. In addition to characterizing seizure phenotypes, the authors also compare the abundance of hilar ectopic granule cells, mossy cells, hilar SOM interneurons, and the degree of neuronal damage between mice with increased neurogenesis (Cre+) vs Cre- controls. The authors find less severe SE and a reduction in chronic seizures in female mice with pre-insult increased adult-born neurons. Immunolabeling experiments show these females also have preservation of hilar mossy cells and somatostatin interneurons, suggesting the pre-insult increase in adult neurogenesis is protective.

Strengths:

(1) The finding that female mice with increased neurogenesis at the time of pilocarpine exposure have fewer seizures despite having increased hilar ectopic granule cells is very interesting.

(2) The work builds nicely on the group's prior studies.

(3) Apparent sex differences are a potentially important finding.

(4) The immunohistochemistry data are compelling.

(5) Good controls for EEG electrode implantation effects.

(6) Nice analysis of most of the SE EEG data.

Weaknesses:

(1) In addition to the Cre- littermate controls, a no Tamoxifen treatment group is necessary to control for both insertional effects and leaky expression of the Nestin-CreERT2 transgene.

About “leaky” expression, we have not found expression to be leaky. We checked by injecting a Cre-dependent virus so that mCherry would be expressed in those cells that had Cre.  The results were published as Supplemental Figure 9 in Jain et al. (2019).

In the revised manuscript we also mention a study that examined three Nestin-CreERT2 mouse lines (Sun et al., 2014). One of the mouse lines was ours. The leaky expression was not in the mouse line we use. We have added these points to the revised manuscript:

Methods, section II starting on line 791:

Although Nestin-Cre-ERT2 mouse lines have been criticized because  they can have leaky expression, the mouse line used in the present study did not (Sun et al., 2014), which we confirmed (Jain et al., 2019).

(2) The authors suggest sex differences; however, experimental procedures differed between male and female mice (as the authors note). Female mice received diazepam 40 minutes after the first pilocarpine-induced seizure onset, whereas male mice did not receive diazepam until 2 hours post-onset. The former would likely lessen the effects of SE on the female mice. Therefore, sex differences cannot be accurately assessed by comparing these two groups, and instead, should be compared between mice with matching diazepam time courses.

We agree that a shorter delay between pilocarpine and diazepam would be likely to lead to less damage. However, the latency from pilocarpine to SE varied, making the time from the onset of SE to diazepam variable. Most of the variability was in females. By timing the diazepam injection differently in males and females, we could make the time from the onset of SE to diazepam similar between females and males. We had added a supplemental figure to show that our approach led to no significant differences between females and males in the latency to SE, time between SE and diazepam injection, and time between pilocarpine and diazepam injection. We also show that Cre+ females and Cre- females were not different in these times, so it could not be related to the neuroprotection of Cre+ females.

Additionally, the authors state that female mice that received diazepam 2 hours post-onset had severe brain damage. This is concerning as it would suggest that SE is more severe in the female than in the male mice.

We regret that our language was misleading. We intended to say females had more morbidity and mortality than males (lack of appetite and grooming, death in the days after SE) when we gave DZP 2 hrs after Pilo. We actually don’t know why because there were no differences in severity of SE. We think the females had worse outcome when they had a short latency to SE.  These females had a longer period of SE before DZP than males, probably leading to worse outcome. To correct this we gave DZP to females sooner. Then morbidity and mortality was improved in females. 

Interestingly, after we did this we saw females did not always have a short latency to SE. We maintained the same regimen however, to be consistent. As the new supplemental figure (above) shows, there were significant sex differences in the latency to SE, time between SE and DZP, and time between pilocarpine and DZP.

(3) Some sample sizes are low, particularly when sex and genotypes are split (n=3-5), which could cause a type II statistical error.

We agree and have noted this limitation in the Discussion:

Additional considerations, starting on line 739:

This study is limited by the possibilities of type II statistical errors in those instances where we divided groups by genotype and sex, leading to comparisons of 3-5 mice/group.

(4) Several figures show a datapoint in the sex and genotype-separated graphs that is missing from the corresponding male and female pooled graphs (Figs. 2C, 2D, 4B).

We are very grateful to the Reviewer for pointing out the errors. They are corrected.

(5) In Suppl Figs. 1B & 1C, subsections 1c and 2c, the EEG trace recording is described as the end of SE; however, SE appears to still be ongoing in these traces in the form of periodic discharges in the EEG.

The Reviewer is correct.  It is a misconception that SE actually ends completely. The most intense seizure activity may, but what remains is abnormal activity that can last for days. Other investigators observe the same and have suggested that it argues against the concept of a silent period between SE and chronic epilepsy. We had discussed this in our prior papers and had referenced how we define SE.  In the revised manuscript we add the information to the Methods section instead of referencing a prior study:

Methods, starting on line 899:

SE duration was defined in light of the fact that the EEG did not return to normal after the initial period of intense activity. Instead, intermittent spiking occurred for at least 24 hrs, as we previously described (Jain et al., 2019) and has been described by others (Mazzuferi et al., 2012; Bumanglag and Sloviter, 2018; Smith et al., 2018). We therefore chose a definition that captured the initial, intense activity. We defined the end of this time as the point when the amplitude of the EEG deflections were reduced to 50% or less of the peak deflections during the initial hour of SE. Specifically, we selected the time after the onset of SE when the EEG amplitude in at least 3 channels had dropped to approximately 2 times the amplitude of the EEG during the first hour of SE, and remained depressed for at least 10 min (Fig. S2 in (Jain et al., 2019). Thus, the duration of SE was defined as the time between the onset and this definition of the "end" of SE.

(6) In Results section II.D and associated Fig.3, what the authors refer to as "postictal EEG depression" is more appropriately termed "postictal EEG suppression". Also, postictal EEG suppression has established criteria to define it that should be used.

We find suppression is typical in studies of ECT or humans (Esmaeili et al., 2023; Gascoigne et al., 2023; Hahn et al., 2023; Kavakbasi et al., 2023; Langroudi et al., 2023; Karl et al., 2024; Vilan et al., 2024; Zhao et al., 2024) and animal research uses the term postictal depression(Kanner et al., 2010; Krishnan and Bazhenov, 2011; Riljak et al., 2012; Singh et al., 2012; Carballosa-Gonzalez et al., 2013; Kommajosyula et al., 2016; Smith et al., 2018; Uva and de Curtis, 2020; Medvedeva et al., 2023). Therefore we think depression is a more suitable term.

The example traces in Fig. 3A and B should also be expanded to better show this potential phenomenon.

We expanded traces in Fig. 3 as suggested. They are in Fig 3A.

(7) In Fig.5D, the area fraction of DCX in Cre+ female mice is comparable to that of Cre- and Cre+ male mice. Is it possible that there is a ceiling effect in DCX expression that may explain why male Cre+ mice do not have a significant increase compared to male Cre- mice?

We thank the Reviewer for the intriguing possibility. We now mention it in the manuscript:

Results, starting on line 456:

It is notable that the Cre+ male mice did not show increased numbers of immature neurons at the time of chronic seizures but Cre+ females did. It is possible that there was a “ceiling” effect in DCX expression that would explain why male Cre+ mice did not have a significant increase in immature neurons relative to male Cre- mice.

(8) In Suppl. Fig 6, the authors should include DCX immunolabeling quantification from conditional Cre+ male mice used in this study, rather than showing data from a previous publication.

We have made this revision.

(9) In Fig 8, please also include Fluorojade-C staining and quantification for male mice.

The additional data for males have been added to part D.

(10) Page 13: Please specify in the first paragraph of the discussion that findings were specific to female mice with pre-insult increases in adult-born neurogenesis.

This has been done.

Minor:

(11) In Fig. 1 and suppl. figure 1, please clarify whether traces are from male or female mice.

We have clarified.

(12) Please be consistent with indicating whether immunolabeling images are from female or male mice.

a. Fig 5B images labeled as from "Cre- Females" and "Cre+ Females".

b. Suppl. Fig 8: Images labeled as "Cre- F" and "Cre+ F".

c. Fig 6: sex not specified.

d. Fig. 7: sex only specified in the figure legend.

e. Fig 8: only female mice were included in these experiments, but this is not clear from the figure title or legend.

We revised all figures according to the comments.

(13) Page 4: the last paragraph of the introduction belongs within the discussion section.

We recognize there is a classic view that any discussion of Results should not be in the Introduction. However, we find that view has faded and more authors make a brief summary statement about the Results at the end of the Introduction. We would like to do so because it allow Readers to understand the direction of the study at the outset, which we find is helpful.

(14) Page 6: The sentence "The data are consistent with prior studies..." is unnecessary.

We have removed the text.

(15) Suppl. Fig 6A: Please include representative images of normal condition DCX immunolabeling.

We have added these data. There is an image of a Cre- female, Cre+ female, Cre- male and Cre+ male in the new figure, Supplemental Figure 6. All mice had tamoxifen at 6 weeks of age and were perfused 6 weeks later. None of the mice had pilocarpine.

(16) In Suppl. Fig 7C, I believe the authors mean "no loss of hilar mossy and SOM cells" instead of "loss of hilar mossy and SOM cells".

This Figure was removed because of the input from Reviewer 1 suggesting it was too speculative.

Reviewer #1 (Recommendations For The Authors):

(1) The main claim of the study is that increasing adult neurogenesis decreases chronic seizures. However, to quantify adult-born neurons, DCX immunoreactivity is used as the sole metric to determine neurogenesis. This is insufficient as changes in DCX-expressing cells could also be an indicator of altered maturation, survival, and/or migration, not proliferation per se. To claim that increasing adult neurogenesis is associated with a reduction of chronic seizures, the authors should perform a pulse/chase (birth dating) experiment with BrdU and co-labeling with DCX.

We think that increased DCX does reflect increased adult neurogenesis. However, we agree that one does not know if it was due to increased proliferation, survival, etc. We also note that this mouse line has been studied thoroughly to show there was increased neurogenesis with BrdU, Ki67 and DCX. We mention that paper in the revised text:

Methods, starting on line 786:

It was shown that after tamoxifen injection in adult mice there is an increase in dentate gyrus neurogenesis based on studies of bromo-deoxyuridine, Ki67, and doublecortin (Sahay et al., 2011).

(2) As mentioned above, analysis of DCX staining alone months after TAM injections is limited. Instead, the cells could be labelled by BrdU prior to TAM injection, following which quantification of BrdU+/Prox1+ cells at 6 weeks post TAM injection should be performed in Cre+ and Cre- mice (males and females) to yield the rate of neurogenesis increase.

We respectfully disagree that birthdating cells is critical. Using DCX staining just before SE, we know the size of the population of cells that are immature at the time of SE. This is what we think is most important because these immature neurons are those that appear to affect SE, as we have already shown.

(3) To confirm the source of the hilar Prox1+ cells, a dual BrdU/EdU labeling approach would be beneficial. BrdU injection could be given before TAM injection and EdU injection before pilocarpine to label different cohorts of neural stem cells. Co-staining with Prox1 at different time points will help in identifying the origin of hilar ectopic cells.

We are grateful for the ideas of the Reviewer. We hesitate to do these experiments now because it seems like a new study to find out where hilar granule cells come from.

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Author response:

The following is the authors’ response to the previous reviews.

Reviewer #1 (Public Review):

Comment 1: One of the only demonstrations of the expression and physiological significance of TRPCs in VTA DA neurons was published by (Rasmus et al., 2011; Klipec et al., 2016) which are not cited in this paper. In their study, TRPC4 expression was detected in a uniformly distributed subset of VTA DA neurons, and TRPC4 KO rats showed decreased VTA DA neuron tonic firing and deficits in cocaine reward and social behaviors. Update: The authors say they have added a discussion of these papers, but I do not see it in the updated manuscript.

We thank the reviewer for the suggestion. The discussion for this has been added (line 557-565).

Comment 2: The authors should report the results (exact data values) of female mice in the results text, or pool the male and female data if the sex differences are not significant.

We agree with reviewer. Some experiments were further redone with female and the data of male and female mice have been reported in the results of text.

Comment 3: The selectivity of drugs should be referred as "selective" rather than "specific". 

Thanks, “specific” has been changed to “selective”.  

Comment 4: Line 62: typo, "substantia nigra". 

Thanks, “substantial nigra” has been changed to “substantia nigra” in line 65.  

Comment 5: Line 77: some new studies suggest that NALCN might have voltage dependency

(rectification).

Thanks, description of NALCN voltage dependence has been corrected in line 81-83.

Comment 6: Line 175: change "less" to "fewer". 

Thanks, “less” has been changed to “fewer”.

Comment 7: Line 299: choose one - "was not ... or" or "was neither ... nor". 

Thanks, this error has been corrected. 

Comment 8: In Figure 1Aii and Figure 3Bi, it was not specified in the results text or figure legend that C1-C5 represent individual cell until the legend for Figure 4.

Thanks, these description about gel have been added in the figure legends. 

Reviewer #2 (Public Review): 

Comment 1: From the previous review, we mentioned that " 'The HCN' as written in line 69 is a bit misleading, as HCN channels in the heart and brain are different members of a family of channels, although as written in the text, it seems that they are identical." This is still the case (now line 73).

We agreed with the reviewer’s comments. The introduction about HCN has been corrected (line 74-78). 

Comment 2: The authors state in line 112 that "most of the experiments were also repeated in female mice" - this is true in the case of most electrophysiological experiments, although not behavioral experiments. Authors should amend the statement in line 112 and clarify in the Discussion section which findings are generalizable between sexes; e.g.:

a.  Discussion of HCN contribution to VTA DA activity (beginning line 453) should clarify male mice. 

b.  Similarly, any discussion of behavioral findings should clarify male mice. 

We agreed with the reviewer’s comments. The sexes of mice used have been noted in the results and discussion. 

Comment 3: The authors' statement in lines 179-183 ("In contrast, fewer GABAergic neuronal markers (Glutamic acid decarboxylase, GAD1/2 and vesicular GABA transporter, VGAT) co-expressed with the DA neurons, which is consistent with previous studies that VTA DA neurons co-expressing GABAergic neuronal markers mainly project to the lateral habenula") is a little confusing - as stated, it seems that the authors are confirming DA/GABA coexpression in VTA-LHb neurons, which is not the case.

We agreed with the reviewer’s comments. We corrected this statement (line 182-186).

Comment 4: Additional information could be included in the Methods section description of Western Blotting procedures - e.g., what thickness of tissue and what size gauge were used to dissect VTA for these experiments?

Thanks. The description of tissue in Western Blotting procedures has been added.

Comment 5:

a. Grammatical errors in line 23 of Abstract (also lines 31-32)

b. "drove" should read "strove" in line 92 

c. Grammatical errors in lines 401, 444, and 448 

We thank the reviewer for pointing out grammatical errors and we corrected them.

Reviewer #3 (Public Review): 

Comment 1: The main strength of this study lies on a comprehensive bottom-up approach ranging from patch-clamp recordings to behavioral tasks. These tasks mainly address anxiety-like behaviors and so-called depression-like behaviors (sucrose choice, forced swim test, tail suspension test). The results gathered by means of these procedures are clearcut. However, the reviewer believes that the authors should be more cautious when interpreting immobility responses to stress (forced swim, tail suspension) as "depression-like" responses. These stress models have been routinely used (and validated) in the past to detect the antidepressant properties of compounds under investigation, which by no means indicates that these are depression models. For readers interested by this debate, I suggest to read e.g. De Kloet and Molendijk (Biol. Pscyhiatry 2021).

We thank the reviewer for the suggestion. We will be more careful and rigorous in the selection of stress models in our subsequent research work.

Editor's note:

Should you choose to revise your manuscript, please include full statistical reporting including exact p-values wherever possible alongside the summary statistics (test statistic and df) and 95% confidence intervals. These should be reported for all key questions and not only when the p-value is less than 0.05.

We have added the full statistical reporting including exact p-values wherever possible alongside the summary statistics (test statistic and df) and 95% confidence intervals into the results and the figure legends of the revised manuscript.

eLife assessment

This important study examined the mechanisms underlying reduced excitability of ventral tegmental area dopamine neurons in mice that underwent a chronic mild unpredictable stress treatment. The authors identify NALCN and TRPC6 channels as key mechanisms that regulate spontaneous firing of ventral tegmental area dopamine neurons and examined their roles in reduced firing in mice that underwent a chronic mild unpredictable stress treatment. The authors' conclusions on neurophysiological data are supported by multiple approaches and are convincing, although the relevance of the behavioral results to human depression remains unclear.

Reviewer #1 (Public Review):

Wang et al., present a paper aiming to identify NALCN and TRPC6 channels as key mechanisms regulating VTA dopaminergic neuron spontaneous firing and investigating whether these mechanisms are disrupted in a chronic unpredictable stress model mouse.

Major strengths:

This paper uses multiple approaches to investigate the role of NALCN and TRPC6 channels in VTA dopaminergic neurons.

Reviewer #2 (Public Review):

This paper describes the results of a set of complementary and convergent experiments aimed at describing roles for the non-selective cation channels NALCN and TRPC6 in mediating subthreshold inward depolarizing currents and action potential generation in VTA DA neurons under normal physiological conditions. In general, the authors have responded satisfactorily to reviewer comments, and the revised manuscript is improved.

Reviewer #3 (Public Review):

The authors of this study have examined which cation channels specifically confer to ventral tegmental area dopaminergic neurones their autonomic (spontaneous) firing properties. Having brought evidence for the key role played by NALCN and TRPC6 channels therein, the authors aimed at measuring whether these channels play some role in so-called depression-like (but see below) behaviors triggered by chronic exposure to different stressors. Following evidence for a down-regulation of TRPC6 protein expression in ventral tegmental area dopaminergic cells of stressed animals, the authors provide evidence through viral expression protocols for a causal link between such a down-regulation and so-called depression-like behaviors. The main strength of this study lies on a comprehensive bottom-up approach ranging from patch-clamp recordings to behavioral tasks. These tasks mainly address anxiety-like behaviors and so-called depression-like behaviors (sucrose choice, forced swim test, tail suspension test). The results gathered by means of these procedures are clearcut.

eLife assessment

This study shows that retinal bipolar cell subtype-specific differences in the size of synaptic ribbon-associated vesicle pools contribute to the transient versus sustained kinetics of the responses of retinal ganglion cells. The findings are important and the data is extensive and solid, however, there is also the possibility that glutamate release could be modulated by the kinetics of presynaptic inhibition at bipolar cell terminals and this may contribute to mediating the transient and/or sustained kinetics of glutamate release. This work will be of broad interest to researchers working on synaptic transmission, retinal signal processing, and sensory neurobiology.

Reviewer #1 (Public Review):

Summary:

In the retina, parallel processing of cone photoreceptor output under bright light conditions dissects critical features of our visual environment and is fundamental to visual function. Cone photoreceptor signals are sampled by several types of bipolar cells and passed onto the ganglion cells. At the output of retinal processing, retinal ganglion cells send about 40 different codes of the visual scene to the brain for further processing. In this study, the authors focus on whether subtype-specific differences in the size of synaptic ribbon-associated vesicle pools of bipolar cells contribute to different retinal ganglion cell (RGC) responses. Specifically, inputs to ON alpha RGCs producing transient versus sustained kinetics (ON-S vs. ON-T, respectively) are compared. The authors first demonstrate that ON-S vs. ON-T RGCs are readily identifiable in a whole mount preparation and respond differently to both static and to a spatially uniform, randomly fluctuating (Gaussian noise) light stimulus. Liner-nonlinear (LN) models were used to estimate the transformation between visual input and excitatory synaptic input for each RGCs; these models suggested the presence of transient versus sustained kinetics already in the excitatory inputs to ON-T and ON-S RGCs. Indeed, the authors show that (glutamatergic) excitatory inputs to ON-S vs. ON-T RGCs are of distinct kinetics. The subtypes of bipolar cells providing input to ON-S are known (i.e., type 6 and 7), but the source of excitatory bipolar inputs to ON-T RGCs needed to be determined. In a tedious process, it is elegantly shown here that ON-T RGCs receive most of their excitatory inputs from type 5 and 6 bipolars. Interestingly, the temporal properties of light-evoked responses of type 5, 6, and 7 bipolars recorded from the somas were indistinguishable and rather sustained, suggesting that the origin of transient kinetics of excitatory inputs to ON-T RGCs suggested by the LN model might be found in the processing of visual signals at the bipolar cell axon terminal. Blocking GABA- or glycinergic inhibitory inputs did not alter the light-evoked excitatory input kinetics to ON-T and ON-S RGCs. Two-photon glutamate sensor imaging revealed significantly faster kinetics of light-evoked glutamate signals at ON-T versus ON-S RGCs. Detailed EM analysis of bipolar cell ribbon synapses onto ON-T and ON-S RGCs revealed fewer ribbon-associated vesicles at ON-T synapses, which is consistent with stronger paired-flash depression of light-evoked excitatory currents in ON-T RGCS versus ON-S RGCs. This study suggests that bipolar subtype-specific differences in the size of synaptic ribbon-associated vesicle pools contribute to transient versus sustained kinetics in RGCs.

Strengths:

The use of multiple, state-of-the-art tools and approaches to address the kinetics of bipolar to ganglion cell synapse in an identified circuit.

Weaknesses:

For the most part, the data in the paper support the conclusions, and the authors were careful to try to address questions in multiple ways. Two-photon glutamate sensor imaging experiment showing that blocking GABA- and glycinergic inhibition does not change the kinetics of light-evoked glutamate signals at ON-T RGCs would strengthen the conclusion that bipolar subtype-specific differences in the size of synaptic ribbon-associated vesicle pools contribute to transient versus sustained kinetics in RGCs.

Reviewer #2 (Public Review):

Summary:

Goal of the study. The authors tried to pinpoint the origins of transient and sustained responses measured at retinal ganglion cells (rgcs), which is the output layer of the retina. Response characteristics of rgcs are used to group them into different types. The diversity of rgc types represents the ability of the retina to transform visual inputs into distinct output channels. They find that the physical dimensions of bipolar cell's synaptic ribbons (specialized release sites/active zones) vary across the different types of cone on-bpcs, in ways that they argue could facilitate transient or sustained release. This diversity of release output is what they argue underlies the differences in on-rgcs response characteristics, and ultimately represents a mechanism for creating parallel cone-driven channels.

Strengths:

The major strengths of the study are the anatomical approaches employed and the use of the "glutamate sniffer" to assay synaptic glutamate levels. The outline of the study is elegant and reflects the strengths of the authors.

Weaknesses:

The major weakness is that the ambitious outline is not matched with a complete set of results, and the set of physiological protocols is disjointed, not sufficient to bridge the systems-level question with the presynaptic release question.

Major comments on the results and suggestions.

The ribbon model of release has been explored for decades and needs to be further adapted to systems-level work. The study under consideration by Kuo et al. takes on this task. Unfortunately, the experimental design does not permit a level of control over presynaptic/bpc behavior that is comparable to earlier studies, nor do they manipulate release in ways that test the ribbon model (i.e., paired recordings or Ribeye-ko). Furthermore, the data needs additional evaluation, and the presentation and interpretations should draw on published biophysical and molecular studies.

To build a ribbon-centric context, consider recent literature that supports the assertion that ribbons play a role in forming AZ release sites and facilitating exocytosis. Reference Ribeye-ko studies. For example, ribbonless bpcs show an 80% reduction in release (Maxeiner et al EMBO J 2016), the ribbonless retina exhibits signaling deficits at the output layer (Okawa et al ...Rieke, ..Wong Nat Comm 2019), and ribbonless rods show an 80% reduction the readily releasable pool (RRP) of SVs (Grabner Moser, elife 2021). In addition, the authors could refer to whole-cell membrane capacitance studies on mammalian rods, cones, and bpcs, because the size of the RRP of SVs scales with the dimensions and numbers of ribbons (total ribbon footprint). For comparison, bipolars see the review by Wan and Heidelberger 2011. For a comparison of mammalian rods and cones, see, rods: Grabner and Moser (2021 eLife), Mueller.. Regus Leidig et al. (2019; J Neurosci) and cones Grabner ...DeVries (Nat Comm 2023). A comparison of cell types shows that the extent of release is (1) proportional to the total size of the ribbon footprint, and (2) less release is witnessed when ribbons are deleted (also see photo ablation studies by Snellman.... And Mehta..Zenisek, Nat Neurosci and Neuron).

Ribbon morphology may change in an activity-dependent manner. The rod ribbon AZ has been reported to lengthen in the dark (Dembla et al 2020), and deletion of the ribbon shortens the length of the AZ (defined by Cav1,4 or RIM2); in addition, the Ribeye-ko AZs fail to change in size with light and dark conditioning. Furthermore, EM studies on rod and cone AZs in light and dark argue that the number of SVs at the base of the ribbon increases in the dark, when PRs are depolarized (see Figure 10, Babai et al 2016 JNeurosci). Lastly, using goldfish Mb1 on-bipolars, Hull et al (2006, J Neurophysio) correlated an increase in release efficiency with an increase in ribbon numbers, which accompanied daylight. >> When release activity is high, ribbon AZ length increases (Dembla, rods), the number of docked SVs increases (Babai, rods cones), and the number of ribbons increases (Hull, diurnal Mb1s).

The results under review, Kuo et al., were attained with SBF-SEM, which has the benefit of addressing large-volume questions as required here, yet it achieves lower spatial resolution than what is attained with TEM tomography and FIB-EM. Ideally, the EM description would include SV size, and the density of ribbon-tethered SVs that are docked at the plasma membrane, because this is where the SVs fuse (additional non-ribbon release sites may also exist? Mehta ... Singer 2014 J Neurosci). Studies by Graydon et al 2011 and 2014 (both in J Neurosci), and Jean ... Moser et al 2018 (eLife) are good examples of quantitative estimates of SVs docking sites at ribbons. SBF-SEM does not allow for an assessment of SVs within 5 nm of the PM, but if the authors can identify the number of SVs that appear within the limit of resolution (10 to 15 nm) from the PM, then this data would be useful. Also, what dimension(s) of the large ribbons make them larger? Typically, ribbons are fixed in height (at least in the outer retina, 200 to 250 nm), but their length varies and the number ribbons per terminal varies. Is the larger ribbon size observed in type 6 bpcs do to longer ribbons, or taller ribbons? A longer ribbon likely has more docked SVs. An additional possibility is that more SVs are about the ribbon-PM footprint, either more densely packed and/or expanding laterally (see definitions in Jean....Moser, elife 2018).

The ribbon literature given above makes the argument that ribbons increase exocytotic output, and morphological studies suggest that release activity enhances 1) ribbon length (Dembla) and 2) the density of SVs near the PM (Babai). These findings could lead one to propose that type 6 bpcs (inputs to On-sustained) are more active than type 5i (feed into On-transient). Here Kuo et al. show that the bpcs have similar Vm (measured from the soma) in response to light stimulation. Does Vm predict release? Not entirely as the authors acknowledge, because: Cav channel properties, SV availability, and negative feedback are all downstream of bpc Vm. The only experiment performed to test downstream factors focused on negative feedback from amacrines. The data presented in Figures 5C-F led me to conclude the opposite of what the authors concluded. My impression is that the T-ON rgc exhibits strong disinhibition when GABA-blockers are applied (the initial phase is greatly increased in amplitude and broadened with the drug), which contrasts with the S-On rgc responses that show a change in the amplitude of the initial phase but not its width (taus would be nice). Here and in many places the authors refer to changes in release kinetics, without implementing a useful description of kinetics. For instance, take the cumulative current (charge) in Figure 5C and fit the control and drug traces to arrive at taus, and their respective amplitudes, and use these values to describe kinetic phases. One final point, the summary in Figure 5D has a p: 0.06, very close to the cutoff for significance, which begs for more than an n = 5. Given that previous studies have shown that bpc output is shaped by immediate msec GABA feedback, in ways that influence kinetic phases of release (..Mb1 bipolars, see Vigh et al 2005 Neuron), more attention to this matter is needed before the authors rule out feedback inhibition in favor of ribbon size. If by chance, type 5i bpcs are under uniquely strong feedback inhibition, then ribbon size may result from less activity, not less output resulting from smaller ribbons.

As mentioned above, the behavior of Cav channels is important here. This is difficult to address with voltage clamps from the soma, especially in the Vm range relevant to this study. Given that it has previously been modeled that the rod bpc to AII pathway adapts to prolonged depolarization of rbcs through downregulating Cav channel-mediated Ca2+ influx (Grimes ....Rieke 2014 Neuron), it seems important for Kou et al to test if there is a difference in Cav regulation between type 6 and 5i bpcs. Ca2+ imaging with a GCaMP strategy (Baden....Lagnado Current Biology, 2011) or filling the presynapse with Ca dyes (see inner hair cells: Ozcete and Moser, EMBO J 2020) would allow for the correlation of [Ca]intra with GluSnf signals (both local readouts).

Stimulation protocol and presentation of Glutamate Sniffer data in Figure 6. In all of your figures where you state steady st as a % of pk amplitude, please indicate in the figure where you estimate steady state. Alternatively, if you take the cumulative dF/F signal, then you can fit the different kinetic phases. From the appearance of the data, the Sustained Glu signals look like square waves (Figure 6B ROI1-4), without a transient at onset, which is not predicted in your ribbon model that assumes different kinetic phases (1. depletion of docked SVs, and 2. refilling and repriming). The Transient responses (Figure 6B ROI5-8) are transient and more compatible with a depressing ribbon scheme. If you take the cumulative, for all of the On-S and compare it to all of the On-T responses, my guess is the cumulative dF/F will be 10 to 20 larger for the S-On. Would you conclude that bpc inputs to On-S (type 6) release 20-fold more SVs per 4 seconds on a per ribbon basis, and does the surface area of the type 6 bpcs account for this difference? From Figures 8B and D, the volume of the ribbon is ~2 fold greater for type 6 vs 5i, but the Surface Area (both faces of ribbon) is more relevant to your model that claims ribbon size is the pivotal factor. If making cumulative traces, and comparisons on an absolute scale is unfounded, then we need to know how to compare different observations. The classic ribbon models always have a conversion factor such as the capacitance of an SV or q size that is used to derive SV numbers from total dCm or Qcontent. See Kim ....et al von Gersdorff, 2023, Cell Reports. Why not use the Gaussian noise stimulus in Fig 6 as in Figure 1 and 2?

Figure 7. What is the recovery time for mammalian cones derived from ribbon-based models? There are estimates from membrane capacitance studies. Ground squirrel cones take 0.7 to 1 sec to recover the ultrafast, primed pool of SVs when probed with a paired-pulse protocol (Grabner ...DeVries 2016, Neuron). Their off-bpcs take anywhere from under 0.2 sec to a second to recover, which is a combination of many synaptic factors (Grabner ...DeVries Nat Comm 2023). Rod On bpcs take over a second (Singer Diamond 2006, reviewed Wan and Heidelberger 2011). In Figure 7B, the recovery time is ~150 ms for the responses measured at rgcs. This brief recovery time is incompatible with existing ribbon models of release. Whole-cell membrane capacitance measurements would be helpful here.

Experimental Suggestion: Add GABA blockers and see if type 5i bpc responds with more release (GluSniff) and prolonged [Ca2+] intra (GCaMP). Compare this to type 6 bpc behavior with GABA/gly blockers. This will rule in or out whether feedback inhibition is involved.

Reviewer #3 (Public Review):

Summary:

Different types of retinal ganglion cell (RGC) have different temporal properties - most prominently a distinction between sustained vs. transient responses to contrast. This has been well established in multiple species, including mice. In general, RGCs with dendrites that stratify close to the ganglion cell layer (GCL) are sustained; whereas those that stratify near the middle of the inner plexiform layer (IPL) are transient. This difference in RGC spiking responses aligns with similar differences in excitatory synaptic currents as well as with differences in glutamate release in the respective layers - shown previously and here, with a glutamate sensor (iGluSnFR) expressed in the RGCs of interest. Differences in glutamate release were not explained by differences in the distinct presynaptic bipolar cells' voltage responses, which were quite similar to one another. Rather, the difference in transient vs. sustained responses seems to emerge at the bipolar cell axon terminals in the form of glutamate release. This difference in the temporal pattern of glutamate release was correlated with differences in the size of synaptic ribbons (larger in the bipolar cells with more sustained responses), which also correlated with a greater number of vesicles in the vicinity of the larger ribbons.

The main conclusion of the study relates to a correlation (because it is difficult to manipulate ribbon size or vesicle density experimentally): the bipolar cells with increased ribbon size/vesicle number would have a greater possibility of sustained release, which would be reflected in the postsynaptic RGC synaptic currents and RGC firing rates. This model proposes a mechanism for temporal channels that is independent of synaptic inhibition. Indeed, some experiments in the paper suggest that inhibition cannot explain the transient nature of glutamate release onto one of the RGC types. Still, it is surprising that such a diverse set of inhibitory interneurons in the retina would not play some role in diversifying the temporal properties of RGC responses.

Strengths:

(1) The study uses a systematic approach to evaluating temporal properties of retinal ganglion cell (RGC) spiking outputs, excitatory synaptic inputs, presynaptic voltage responses, and presynaptic glutamate release. The combination of these experiments demonstrates an important step in the conversion from voltage to glutamate release in shaping response dynamics in RGCs.

(2) The study uses a combination of electrophysiology, two-photon imaging, and scanning block-face EM to build a quantitative and coherent story about specific retinal circuits and their functional properties.

Weaknesses:

(1) There were some interesting aspects of the study that were not completely resolved, and resolving some of these issues may go beyond the current study. For example, it was interesting that different extracellular media (Ames medium vs. ACSF) generated different degrees of transient vs. sustained responses in RGCs, but it was unclear how these media might have impacted ion channels at different levels of the circuit that could explain the effects on temporal tuning.

(2) It was surprising that inhibition played such a small role in generating temporal tuning. At the same time, there were some gaps in the investigation of inhibition (e.g., IPSCs were not measured in either of the RGC types; pharmacology was used to investigate responses only in the transient RGCs).

(3) There could be additional discussion and references to the literature describing several topics, including: temporal dynamics of glutamate release at different levels of the IPL; previous evidence that release sites from a single presynaptic neuron can differ in their temporal properties depending on the postsynaptic target; previous investigations of the role of inhibition in temporal tuning within retinal circuitry.

eLife assessment

This important study examined the dynamics of attentional reorientation in working memory by assessing alpha-band lateralization in EEG recordings and saccade bias and provides convincing evidence for a second stage of internal attentional deployment during WM. This work provides novel insights into the dynamic mechanism in WM and will be of broad interest and impact to cognitive neuroscience, including attention and working memory. Performing additional analysis to disentangle the roles of saccade and micro-saccade and to show behavioral relevance would further strengthen the conclusion.

Reviewer #1 (Public Review):

In the study "Re-focusing visual working memory during expected and unexpected memory tests" by Sisi Wang and Freek van Ede, the authors investigate the dynamics of attentional re-orienting within visual working memory (VWM). Utilizing a robust combination of behavioral measures, electroencephalography (EEG), and eye tracking, the research presents a compelling exploration of how attention is redirected within VWM under varying conditions. The research question addresses a significant gap in our understanding of cognitive processes, particularly how expected and unexpected memory tests influence the focus and re-focus of attention. The experimental design is meticulously crafted, enabling a thorough investigation of these dynamics. The figures presented are clear and effectively illustrate the findings, while the writing is concise and accessible, making the complex concepts understandable. Overall, this study provides valuable insights into the mechanisms of visual working memory and attentional re-orienting, contributing meaningfully to the field of cognitive neuroscience. Despite the strengths of the manuscript, there are several areas where improvements could be made.

Microsaccades or Saccades?

In the manuscript, the terms "microsaccades" and "saccades" are used interchangeably. For instance, "microsaccades" are mentioned in the keywords, whereas "saccades" appear in the results section. It is crucial to differentiate between these two concepts. Saccades are large, often deliberate eye movements used for scanning and shifting attention, while microsaccades are small, involuntary movements that maintain visual perception during fixation. The authors note the connection between microsaccades and attention, but it is not well-recognized that saccades are directly linked to attention. Despite the paradigm involving a fixation point, it remains unclear whether large eye movements (saccades) were removed from the analysis. The authors mention the relationship between microsaccades and attention but do not clarify whether large eye movements (saccades) were excluded from the analysis. If large eye movements were removed during data processing, this should be documented in the manuscript, including clear definitions of "microsaccades" and "saccades." If such trials were not removed, the contribution of large eye movements to the results should be shown, and an explanation provided as to why they should be considered.

Alpha Lateralization in Attentional Re-orienting

In the attentional orienting section of the results (Figure 2), the authors effectively present EEG alpha lateralization results with time-frequency plots and topographic maps. However, in the attentional re-orienting section (Figure 3), these visualizations are absent. It is important to note that the time period in attentional orienting differs from attentional re-orienting, and consequently, the time-frequency plots and topographic maps may also differ. Therefore, it may be invalid to compute alpha lateralization without a clear alpha activity difference. The authors should consider including time-frequency plots and topographic maps for the attentional re-orienting period to validate their findings.

Onset and Offset Latency of Saccade Bias

The use of the 50% peak to determine the onset and offset latency of the saccade bias is problematic. For example, if one condition has a higher peak amplitude than another, the standard for saccade bias onset would be higher, making the observed differences between the onset/offset latencies potentially driven by amplitude rather than the latencies themselves. The authors should consider a more robust method for determining saccade bias onset and offset that accounts for these amplitude differences.

Control Analysis for Trials Not Using the Initial Cue

The control analysis for trials where participants did not use the initial cue raises several questions:

(1) The authors claim that "unlike continuous alpha activity, saccades are events that can be classified on a single-trial level." However, alpha activity can also be analyzed at the single-trial level, as demonstrated by studies like "Alpha Oscillations in the Human Brain Implement Distractor Suppression Independent of Target Selection" by Wöstmann et al. (2019). If single-trial alpha activity can be used, it should be included in additional control analyses.

(2) The authors aimed to test whether the re-orienting signal observed after the test is not driven exclusively by trials where participants did not use the initial cue. They hypothesized that "in such a scenario, we should only observe attention deployment after the test stimulus in trials in which participants did not use the preceding retro cue." However, if the saccade bias is the index for attentional deployment, the authors should conduct a statistical test for significant saccade bias rather than only comparing toward-saccade after-cue trials with no-toward-saccade after-cue trials. The null results between the two conditions do not immediately suggest that there is attention deployment in both conditions.

(3) Even if attention deployment occurs in both conditions, the prolonged re-orienting effect could also be caused by trials where participants did not use the initial cue. Unexpected trials usually involve larger and longer brain activity. The authors should perform the same analysis on the time after the removal of trials without toward-saccade after the cue to address this potential confound.

Reviewer #2 (Public Review):

Summary:

This study utilized EEG-alpha activity and saccade bias to quantify the spatial allocation of attention during a working memory task. The findings indicate a second stage of internal attentional deployment following the appearance of a memory test, revealing distinct patterns between expected and unexpected test trials. The spatial bias observed during the expected test suggests a memory verification process, whereas the prolonged spatial bias during the unexpected test suggests a re-orienting response to the memory test. This work offers novel insights into the dynamics of attentional deployment, particularly in terms of orienting and re-orienting following both the cue and memory test.

Strengths:

The inclusion of both EEG-alpha activity and saccade bias yields consistent results in quantifying the attentional orienting and re-orienting processes. The data clearly delineate the dynamics of spatial attentional shifts in working memory. The findings of a second stage of attentional re-orienting may enhance our understanding of how memorized information is retrieved.

Weaknesses:

Although analyses of neural signatures and saccade bias provided clear evidence regarding the dynamics of spatial attention, the link between these signatures and behavioral performance remains unclear. Given the novelty of this study in proposing a second stage of 'verification' of memory contents, it would be more informative to present evidence demonstrating how this verification process enhances memory performance.

Reviewer #3 (Public Review):

Summary:

Wang and van Ede investigate whether and how attention re-orients within visual working memory following expected and unexpected centrally presented memory tests. Using a combination of spatial modulations in neural activity (EEG-alpha lateralization) and gaze bias quantified as time courses of microsaccade rate, the authors examined how retro cues with varying levels of reliability influence attentional deployment and subsequent memory performance. The conclusion is that attentional re-orienting occurs within visual working memory, even when tested centrally, with distinct patterns following expected and unexpected tests. The findings provide new value for the field and are likely of broad interest and impact, by highlighting working memory as an action-bound process (in)dependent on (an ambiguous) past.

Strengths:

The study uniquely integrates behavioral data (accuracy and reaction time), EEG-alpha activity, and gaze tracking to provide a comprehensive analysis of attentional re-orienting within visual working memory. As typical for this research group, the validity of the findings follows from the task design that effectively manipulates the reliability of retro cues and isolates attentional processes related to memory tests. The use of well-established markers for spatial attention (i.e. alpha lateralization) and more recently entangled dependent variable (gaze bias) is commendable. Utilizing these dependent metrics, the concise report presents a thorough analysis of the scaling effects of cue reliability on attentional deployment, both at the behavioral and neural levels. The clear demonstration of prolonged attentional deployment following unexpected memory tests is particularly noteworthy, although there are no significant time clusters per definition as time isn't a factor in a statistical sense, the jackknife approach is convincing. Overall, the evidence is compelling allowing the conclusion of a second stage of internal attentional deployment following both expected and unexpected memory tests, highlighting the importance of memory verification and re-orienting processes.

Weaknesses:

I want to stress upfront that these weaknesses are not specific to the presented work and do not affect my recommendation of the paper in its present form.

The sample size is consistent with previous studies, a larger sample could enhance the generalizability and robustness of the findings. The authors acknowledge high noise levels in EEG-alpha activity, which may affect the reliability of this marker. This is a general issue in non-invasive electrophysiology that cannot be handled by the authors but an interested reader should be aware of it. Effectively, the sensitivity of the gaze analysis appears "better" in part due to the better SNR. The latter also sets the boundaries for single-tiral analyses as the authors correctly mention. In terms of generalizability, I am convinced that the main outcome will likely generalize to different samples and stimulus types. Yet, as typical for the field future research could explore different contexts and task demands to validate and extend the findings. The authors provide here how and why (including sharing of data and code).

eLife assessment

This valuable study investigates the contribution of far-red light photo-acclimated cyanobacteria to primary production in intertidal beachrock habitats. Though the study presents solid evidence, the text would benefit from an improved discussion section and some additional methodological details.

Reviewer #1 (Public Review):

Summary:

Mosshammer et al. studied the oxygenic photosynthetic productivity of beachrock samples containing cyanobacteria with different pigment compositions. The use of longer wavelength absorbing chlorophylls in some cyanobacteria (chlorophylls d and f) allows their photosystems to use light further in the red than canonical chlorophyll a photosystems. As such, their distribution in visible light-shaded environments, such as the beachrock studied by Mosshammer et al., allows them to perform oxygenic photosynthesis using wavelengths not capable of driving photosynthesis in most cyanobacteria, algae, or plants.

By adapting measuring systems they have previously used to study these types of beachrock samples, the authors attempt to mimic a more natural light penetration through the beachrock in order to measure oxygen production. By doing so with different wavelengths and intensities, the authors are able to show that far-red light-driven oxygen production is potentially capable of driving high levels of gross primary production.

Strengths:

The manuscript builds on previous measurement techniques used by the authors while focussing on illumination from the top of a sample rather than the specific microbial layers themselves. This provides a more environmentally realistic understanding of the beachrock community, as well as far-red light-driven photosynthesis.

The manuscript benefits from using previously defined methods to further characterize complex environmental samples.

Weaknesses:

The manuscript suffers from a lack of discussion and interpretation of the findings, and as such is more of a report.

Using the envionmental beachrock samples has inherent complications, from the variation in rock morphology, to the microbial community composition of different samples as well as within a single sample. It would benefit the authors to discuss these technical difficulties in more detail, as the light penetration through the beachrock is likely greatly limiting measurements of chlorophyll f and/or chlorophyll d-driven photosynthesis in the beachrock.

This can be seen in the different luminescence measurements (Figure 2 and supplements), that the different samples have clear differences in far-red light-driven oxygen production. While the BLACK sample produces oxygen with 740nm LED filtered with a NIR-75N filter, neither of the other two samples produce measureable oxygen under this condition. Conversely, this sample results in the lowest level of gross photosynthesis when measuring dissolved oxygen. A more detailed discussion of the variation between and within samples and measurements would benefit the overall results of the manuscript.

The PINK beachrock sample has the highest level of chlorophyll d per chlorophyll a. As FaRLiP cyanobacteria only incorporate 1 chlorophyll d per photosystem II, and none in photosytem I, is there a (relatively) high composition of Acaryochloris species in the PINK sample? If normalized to the reflectance minima can more distinct populations be identified?

For Figure 1, multiple points should be clarified. The first is that the HPLC methods are estimates of concentrations, as the extinction coefficients are not correct for the solvent solution for which the pigments elute, and are likely to be differently incorrect for each pigment. This results in quantitatively incorrect data, but qualitative comparisons between samples likely remain valid. Secondly, the pigment concentrations can also be misleading. Within the cyanobacterial cells, photosystem I harbors approximately 3 times as many chlorophylls as photosystem II. While the community numbers and photosystem stoichiometry are not necessarily relevant to the current study, the red shift in absorbance between photosystem II and photosystem I is of importance for the measurements performed. How cyanobacterial cells with differing concentrations of photosystems will absorb the red tail of the far-red LEDs, as well as impact the light penetration would be a useful discussion point.

The different samples used are from varying beachrock zonations but have the same chlorophyll f per chlorophyll a concentrations. A discussion of why this might be would be useful.

For the luminescence measurements (Figure 2 and supplements), no oxygen production is seen in the BROWN or PINK beachrock samples when the 740nm LED is filtered with a NIR-75N filter. This is likely due to multiple factors (low initial intensity compounded by penetration depth, community composition, etc.) but should be discussed. While the authors say that Chrooccidiopsis species dominate the samples, variation of absorbance between different chlorophyll f containing cyanobacteria has also been measured (see Tros et al. 2021, Chem), and the extent to which even chlorophyll f species extend into the far-red varies. Discussions about these implications would help with their characterization of the luminescence data. While the authors discuss that based on their respiration measurements the oxygen may be being consumed, resulting in an inability to measure it (lines 147-150), other explanations are clearly viable.

For the luminescence measurements, no oxygen production is discernable in the endolithic region when excited with visible light, which is at a much stronger intensity than the near-infrared light used. However, both Acaryochloris and chlorophyll f cyanobacteria are capable of driving photosynthesis with visible light. As the intensities used are much brighter than for the NIR measurements, presumably generated oxygen would be higher than what could be immediately consumed by respiration. It is important that the authors address this.

A highlighted point by the authors is the >20% of photosynthesis driven by NIR in the beachrock at comparable irradiation. However, this statement is deceiving for multiple reasons.<br /> (1) The irradiation is likely not comparable for what is reaching the cells. This is not a problem per se as illumination from above is the point, but does skew the interpretation.<br /> (2) The >20% value comes from the maximum amount of gross photosynthesis driven by NIR at ~1400 umol photons m-2s-1, whereas at other comparable illuminations the value is much, much lower (<1%). A likely interpretation of such data is that while the chlorophyll f endolithic layer is capable of producing a relatively large amount of oxygen, it is likely far less productive under most illuminations, though not zero.

The authors have the difficult task of weaving in results from laboratory, uniculture or isolated photosystem measurements with their environmental-based results. This is especially clear in lines 172-183. While the authors are correct that measurements of trapping times in chlorophyll f containing photosystems have been measured and are slower in chlorophyll f photosystem II and photosystem I relative to all chlorophyll a photosystems, the quantum yield for trapping remains high in chlorophyll f photosystem I (Tros et al. 2021, Chem). The quantum yield of trapping for chlorophyll f photosystem II is much lower for chlorophyll f than chlorophyll a complex, though improved by the attachment of phycobilisomes. However, these are intrinsic physical properties of the complexes that are not modulated in response to the environments. This could be interpreted that at low photon flux densities as measured in these experiments, the endolithic near infrared-driven oxygen production could be limited by an overall lower quantum efficiency of trapping the captured light and thus minimizing photosynthetic productivity relative to a theoretical level based on the efficiency of the chlorophyll a photosystem II. How the variations in intensity and spectral composition impact the cyanobacterial community likely involves many other factors and has not been addressed (though see Nurnberg et al. 2018, Science and Viola et al. 2022 eLife for further discussions).

Reviewer #2 (Public Review):

The authors investigate the role of near-infrared photosynthesis in primary production across three beachrock communities. This work is particularly pertinent as more cyanobacteria with far-red light acclimation capacities are discovered, underscoring the need to assess their contributions to primary production. However, the manuscript is currently very difficult to follow due to unclear correlations between the text and figures and the samples analyzed in the different experiments.. Additional explanations would also enhance clarity. For example, it would be beneficial for the authors to better define the three communities, as distinctions are not apparent. Another example is the pigment analysis, where the extinction coefficients for pigments vary in different solvents. Quantification by chromatography should use calibration curves for all pigments, not just Chl a, as is currently done. Pigments can be easily purified from cyanobacteria for this purpose.

Reviewer #3 (Public Review):

Summary:

On islands in the pacific, beachrock occurs near high tide level, composed of calcareous material. The surface of the beach rock is colonised by cyanobacteria and some eukaryotic algae. On Heron Island on the Southern Great Barrier Reef, beach rock occurs on the north and south side of the island in continuous slabs, which slope gently upwards toward the island. Thus the upper beach rock is only inundated at extreme high tides. On the south side, the major photosynthetic organism is a cyanobacterium Chroococcidiopsis, which forms tough smooth mats over all the beach rock. This cyanobacterium belongs to a newly discovered class called FaRLiP photosynthesisers, which carry out conventional photosynthesis under visible radiation using chlorophyll a (Chl a) but which deactivate most of the Chl a under near infra -red radiation (NIR) and produce chlorophyll f and chlorophyll d which can absorb NIR (700 - 760 nm). These NIR Chl molecules are repositioned in the reaction centres. In addition, an NIR-activated allophycocyanin (a phycobiliprotein) is synthesised and placed in the reaction centres. These FaRLiP cyanobacteria can carry out photosynthesis and primary production when placed under NIR. Here it is shown that in the mats of Chroococcidiopsis on the beach rock the upper layers carry out conventional photosynthesis while the lower layers carry out FaRLiP photosynthesis. It is shown that the FaRLiP-activated lower layers can produce up to 20% of the total photosynthetic primary production.

Strengths:

The authors have researched sections of beachrock obtained from the beach rock on Heron Island. The Beach Rock on Heron Island occurs on both sides of the Island lying in a semi-horizontal position slightly sloping upwards toward the Island. At normal high tide, only the upper parts are not submerged. Black crusts occur in the uppermost parts of the beachrock. Brown crusts occur in the intermediate sites and pink crusts occur at the lowest part of the beachrock.

The crusts are made up largely of cyanobacteria and the major component is a cyanobacterium of one species, tentatively identified by shape, pigmentation, and partial DNA analysis as Chroococcidiopsis.

In this investigation sections of the beach rock from different levels have been analysed using three techniques:

(1) Hyperspectral analysis to determine the layout of pigmented cells and their spectra.

(2) Bioluminescence to determine the spectra of the cells in the sections.

(3) Oxygen analysis, using luminescence lifetime imaging on special films closely applied to vertical sections of the beachrock.

(4) Oxygen production from the surface of three-dimensional blocks of beach rock, illuminated with white light or Near Infra Red (NIR) radiation, from above.

In addition, pigmentation has been analysed by High Performance Liquid Chromatography (HPLC).

These techniques allow the following conclusions:

(1) Scytonemin is a main screening compound for UV irradiation.

(2) Carotenoids also play a part in screening from UV and probably visible radiation.

(3) The cyanobacteria occur near the rock surface and contain Chl a plus some Chl f and a small amount of Chl d.

(4) HPLC pigment analysis confirms the presence of Chl a plus Chl f and a small amount of Chl d.

(5) The deeper layer with FaRLiP cyanobacteria produces oxygen under both visible light and NIR irradiation, with different P vs I curves.

(6) Using the oxygen chamber to measure oxygen exchange above the beach rock surface, it was shown that high respiration meant that only with the brown samples was significant oxygen released to the water column at lower light levels, i.e. respiration accounted for most of the primary production of oxygen except at the highest visible light intensities. And with NIR much lower levels of oxygen production only breaking compensation significantly in the brown samples.

(7) FaRLiP primary production was significant in the deeper layer.

The major new conclusion from these studies is that FaRLiP photosynthesis is a significant factor in this biofilm, and possibly other biofilms. Visible light is mostly absorbed in the upper layers and NIR reaching the lower layers induces FaRLiP photosynthesis and primary production, which can be up to 20% of the total primary production of the film.

Weaknesses:

The techniques are sufficient to justify the conclusions, especially the new result that the FaRLiP photosynthesis deeper in the films is surprisingly active with relatively high primary productivity. This is an important conclusion but it must be realised that there is some way to go to polish up the results and gain more quantitative results.

Firstly the beachrock is a heterogeneous material. So cutting a section leaves a non-homogeneous surface where various sand grains are removed, cut, or not removed. This means that when applying a luminescence film, the results are dependent on the uniformity of the surface or rather the lack of conformity. This needs to be taken into consideration in future studies.

Furthermore, previous papers have revealed that pits in the beach rock are important sites for FaRLiP cyanobacteria and the paper needs to make clear that these pits were avoided here.

Secondly, while Chroococcidiopsis is the major alga/cyanobacterium present, other algae/cyanobacteria are present and their presence needs to be factored into the results. In this regard we need more microscopic images of the surface and cross-sections of the beachrock, to reveal the nature of the bacterial and algal organisms.

Thirdly, it is not clear from this paper how far the identification of Chroococcidiopsis is firm. Presumably preliminary DNA analyses have been carried out on tell-tale genes (rRNA?). At some stage, a complete genome will be needed. Mention should be made about what has been done and what is contemplated.

Fourthly, the acclimation to FaRLiP is time-dependent. How long does it take in these beach rock sections? And has sufficient notice been taken of this time-dependent process?

Fifthly, FaRLiP is a sophisticated system as shown by Mascoli et al, 2022. It is activated in NIR by red-shifted allophycocyanin. It is also dependent on the allocation of Chl f and Chl d to special positions in the reaction centre. All this may take some time and be light-dependent. This may explain the curious increase in the slopes of light vs productivity of Fig 4 (Pink and Black) for NIR light.

The fifth point needs to be taken into account in any rewrite of the paper. The authors assume that the upwardly sloping P vs I curve is explained as follows:<br /> "This can be explained by the light attenuation due to scattering and absorption in the compacted beachrock biofilm, which prevented saturation of NIR-driven photosynthesis in the endolithic layer even at levels of incident light similar to solar irradiation on mid-day exposed beachrock."

Activation of the FaRLiP system also needs to be considered.

Author response:

The following is the authors’ response to the current reviews.

We thank the Reviewers and Editors for the constructive comments, which we believe have significantly improved the quality of our manuscript.

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The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

(1) With respect to the predictions, the authors propose that the subjects, depending on their linguistic background and the length of the tone in a trial, can put forward one or two predictions. The first is a short-term prediction based on the statistics of the previous stimuli and identical for both groups (i.e. short tones are expected after long tones and vice versa). The second is a long-term prediction based on their linguistic background. According to the authors, after a short tone, Basque speakers will predict the beginning of a new phrasal chunk, and Spanish speakers will predict it after a long tone.

In this way, when a short tone is omitted, Basque speakers would experience the violation of only one prediction (i.e. the short-term prediction), but Spanish speakers will experience the violation of two predictions (i.e. the short-term and long-term predictions), resulting in a higher amplitude MMN. The opposite would occur when a long tone is omitted. So, to recap, the authors propose that subjects will predict the alternation of tone durations (short-term predictions) and the beginning of new phrasal chunks (long-term predictions).

The problem with this is that subjects are also likely to predict the completion of the current phrasal chunk. In speech, phrases are seldom left incomplete. In Spanish is very unlikely to hear a function-word that is not followed by a content-word (and the opposite happens in Basque). On the contrary, after the completion of a phrasal chunk, a speaker might stop talking and a silence might follow, instead of the beginning of a new phrasal chunk.

Considering that the completion of a phrasal chunk is more likely than the beginning of a new one, the prior endowed to the participants by their linguistic background should make us expect a pattern of results actually opposite to the one reported here.

We thank the Reviewer #1 for this pertinent comment and the opportunity to address this issue. A very similar concern was also raised by Reviewer #2. Below we try to clarify the motivations that led us to predict that the hypothesized long-term predictions should manifest at the onset (and not within or the end) of a perceptual chunk. 

Reviewers #1 and #2 contest a critical assumption of our study i.e., the fact that longterm predictions should occur at the beginning of a rhythmic chunk as opposed to its completion. They also contest the prediction deriving from this view i.e., omitting the first sound in a perceptual chunk (short for Spanish, long for Basque) would lead to larger error responses than omitting a later element. They suggest an alternative view: the omission of tones at the end of a perceptual rhythmic chunk would evoke larger error responses than omissions at its onset, as subjects are more likely to predict the completion of the chunk than its beginning. This view predicts an interaction effect in the opposite direction of our findings. 

While we acknowledge this as a plausible hypothesis, we believe that the current literature provides strong support for our view. Indeed, many studies in the rhythm and music perception literature have investigated the ERP responses to deviant sounds and omissions placed at different positions within rhythmic patterns (e.g., Ladinig et al., 2009; Bouwer et al., 2016; Brochard et al., 2003; Potter et al., 2009; Yabe et al., 2001). For instance, Lading et al., 2009 presented participants with metrical rhythmical sound sequences composed of eight tones. In some deviant sequences, the first or a later tone was omitted. They found that earlier omissions elicited earlier and higher-amplitude MMN responses than later omissions (irrespective of attention). Overall, this and other studies showed that the amplitude of ERP responses are larger when deviants occur at positions that are expected to be the “start” of a perceptual group - “on the beat” in musical terms - and decline toward the end of the chunk. According to some of these studies, the first element of a chunk is particularly important to track the boundaries of temporal sequences, which is why more predictive resources are invested at that position. We believe that this body of evidence provides robust bases for our hypotheses and the directionality of our predictions.

An additional point that should be considered concerns the amplitude of the prediction error response elicited by the omission. From a predictive coding perspective, the omission of the onset of a chunk should elicit larger error responses because the system is expecting the whole chunk (i.e., two tones/more acoustic information). On the other hand, the omission of the second tone - in the transition between two tones within the chunk - should elicit a smaller error response because the system is expecting only the missing tone (i.e. less acoustic information). 

Given the importance of these points, we have now included them in the updated version of the paper, in which we try to better clarify the rationale behind our hypothesis (see Introduction section, around the 10th paragraph).

(2) The authors report an interaction effect that modulates the amplitude of the omission response, but caveats make the interpretation of this effect somewhat uncertain. The authors report a widespread omission response, which resembles the classical mismatch response (in MEG) with strong activations in sensors over temporal regions. Instead, the interaction found is circumscribed to four sensors that do not overlap with the peaks of activation of the omission response.

We thank the Reviewer for this comment. As mentioned in the provisional response, the approach employed to identify the presence of an interaction effect was conservative: We utilized a non-parametric test on combined gradiometers data, without making a priori assumptions about the location of the effect, and employed small cluster thresholds (cfg.clusteralpha = 0.05) to increase the chances of detecting highly localized clusters with large effect sizes. The fact that the interaction effect arises in a relatively small cluster of sensors does not alter its statistical robustness. It should be also considered that in the present analyses we focused on planar gradiometer data that, compared to magnetometers and axial gradiometers, present more fine-grained spatial resolution and are more suited for picking up relatively small effects. 

The partial overlap of the cluster with the activation peaks may simply reflect the fact that different sources contribute to the generation of the omission-MMN, which has been reported in several studies (e.g., Zhang et al., 2018; Ross & Hamm, 2020).  We value the Reviewer’s input and are grateful for the opportunity to address these considerations.

Furthermore, the boxplot in Figure 2E suggests that part of the interaction effect might be due to the presence of two outliers (if removed, the effect is no longer significant). Overall, it is possible that the reported interaction is driven by a main effect of omission type which the authors report, and find consistently only in the Basque group (showing a higher amplitude omission response for long tones than for short tones). Because of these points, it is difficult to interpret this interaction as a modulation of the omission response.

We thank the Reviewer for the comment and appreciate the opportunity to address these concerns. We have re-evaluated the boxplot in Figure 2E and want to clarify that the two participants mentioned by Reviewer #1, despite being somewhat distant from the rest of the group, are not outliers according to the standard Tukey’s rule. As shown in the figure below, no participant fell outside the upper (Q3+1.5xIQR) and lower whiskers (Q1-1.5xIQR) of the boxplot. 

Moreover, we believe that the presence of a main effect of omission type does not impact the interpretation of the interaction, especially considering that these effects emerge over distinct clusters of channels (see Fig. 1 C; Supplementary Fig. 2 A). 

Based on these considerations - and along with the evidence collected in the control study and the source reconstruction data reported in the new version of the manuscript - we find it unlikely that the interaction effect is driven by outliers or by a main effect of omission type. We appreciate the opportunity provided by the Reviewer to address these concerns, as we believe they strengthen the claim that the observed effect is driven by the hypothesized long-term linguistic priors rather than uncontrolled group differences.

Author response image 1.

It should also be noted that in the source analysis, the interaction only showed a trend in the left auditory cortex, but in its current version the manuscript does not report the statistics of such a trend.

We  appreciate  the  Reviewer’s  suggestion  to  incorporate  more comprehensive source analyses. In the new version of the paper, we perform new analyses on the source data using a new Atlas with more fine-grained parcellations of the regions of interests (ROIs) (Brainnetome atlas; Fan et al., 2016) and focusing on peak activity to increase response’s sensitivity in space and time. We therefore invite the Reviewer to read the updated part on source reconstruction included in the Results and Methods sections of the paper.  

Reviewer #1 (Recommendations For The Authors):

While I have described my biggest concerns with respect to this work in the public review, here I list more specific points that I hope will help to improve the manuscript. Some of these are very minor, but I hope you will still find them constructive. 

(1) I understand the difficulties implied in recruiting subjects from two different linguistic groups, but with 20 subjects per group and a between-groups design, the current study is somewhat underpowered. A post-hoc power analysis shows an achieved power of 46% for medium effect sizes (d = 0.5, and alpha = 0.05, one-sided test). A sensitivity analysis shows that the experiment only has 80% power for effect sizes of d = 0.8 and above. It would be important to acknowledge this limitation in the manuscript. 

We thank the Reviewer for reporting these analyses. It must be noted that our effect of interest was based on Molnar et al.’s (2016) behavioral experiment, in which a sample size of 16 subjects per group was sufficient to detect the perceptual grouping effect. In Yoshida et al., (2010), the perceptual grouping effect emerged with two groups of 20 7–8-month-old Japanese and English-learning infants. Based on these previous findings, we believe that a sample size of 20 participants per group can be considered appropriate for the current MEG study. We clarified these aspects in the Participants section of the manuscript, in which we specified that previous behavioral studies detected the perceptual grouping with similar sample sizes. Moreover, to acknowledge the limitation highlighted by the Reviewer, we also include the power and sensitivity analysis in a note in the same section (see note 2 in the Participants section).

(2) All the line plots in the manuscript could be made much more informative by adding 95% CI bars. For example, in Figure 4A, the omission response for the long tone departs from the one for the short tone very early. Adding CIs would help to assess the magnitude of that early difference. Error bars are present in Figure 3, but it is not specified what these bars represent. 

Thanks for the comments. We added the explanation of the error bars in the new version of Figure 3. For the remaining figures, we prefer maintaining the current version of the ERF, as the box-plots accompanying them provide information about the distribution of the effect across participants.

(3) In the source analysis, there is only mention of an interaction trend in the left auditory cortex, but no statistics are presented. If the authors prefer to mention such a trend, I think it would be important to provide its stats to allow the reader to assess its relevance. 

We performed new analysis on the source data, all reported in the updated version of the manuscript.

(4) In the discussion section, the authors refer to the source analysis and state that "the interaction is evident in the left". But if only a statistical trend was observed, this statement would be misleading. 

We agree with this comment. We invite the Reviewer to check the new part on source reconstruction, in which contrasts going in the same direction of the sensor level data are performed.

(5) In the discussion the authors argue that "This result highlights the presence of two distinct systems for the generation of auditory" that operate at different temporal scales, but the current work doesn't offer evidence for the existence of two different systems. The effects of long-term priors and short-term priors presented here are not dissociated and instead sum up. It remains possible that a single system is in place, collecting statistics of stimuli over a lifetime, including the statistics experienced during the experiment. 

Thanks for pointing that out. We changed the sentence above as follows: “This result highlights the presence of an active predictive system that relies on natural sound statistics learned over a lifetime to process incoming auditory input”.

(6) In the discussion, the authors acknowledge that the omission response has been interpreted both as pure prediction and as pure prediction error. Then they declare that "Overall, these findings are consistent with the idea that omission responses reflect, at least in part, prediction error signals.". However an argument for this statement is not provided. 

Thanks for pointing out this lack of argument. In the new version of the manuscript, we explained our rationale as follows: “Since sensory predictive signals primarily arise in the same regions as the actual input, the activation of a broader network of regions in omission responses compared to tones suggests that omission responses reflect, at least in part, prediction error signals”.

(7) In the discussion the authors present an alternative explanation in which both groups might devote more resources to the processing of long events, because these are relevant content words. Following this, they argue that "Independently on the interpretation, the lack of a main effect of omission type in the control condition suggests that the long omission effect is driven by experience with the native language." However as there was no manipulation of duration in the control experiment, a lack of the main effect of omission type there does not rule out the alternative explanation that the authors put forward. 

This is correct; thanks for noticing it. We removed the sentence above to avoid ambiguities.

Minor points: 

(8) The scale of the y-axis in Figure 2C might be wrong, as it goes from 9 to 11 and then to 12. If the scale is linear, the top value should be 13, or the bottom value should be 10. 

Figure 2C has been modified accordingly, thanks for noticing the error.

(9) There is a very long paragraph starting on page 7 and ending on page 8. Toward the end of the paragraph, the analysis of the control condition is presented. That could start a new paragraph.

Thanks for the suggestion. We modified the manuscript as suggested.

Reviewer #2 (Public Review):

(1) Despite the evidence provided on neural responses, the main conclusion of the study reflects a known behavioral effect on rhythmic sequence perceptual organization driven by linguistic background (Molnar et al. 2016, particularly). Also, the authors themselves provide a good review of the literature that evidences the influence of longterm priors in neural responses related to predictive activity. Thus, in my opinion, the strength of the statements the authors make on the novelty of the findings may be a bit far-fetched in some instances.

Thanks for the suggestion. A similar point was also advanced by Reviewer 1. In general, we believe our work speaks about the predictive nature of such experiencedependent  effects, and show that these linguistic priors shape sensory processes at very early stages. This is discussed in the sixth and seventh paragraphs of the Discussion section. In the new version of the article, we modified some statements and tried to make them more coherent with the scope of the present work. For instance, we changed "This result highlights the presence of two distinct systems for the generation of auditory predictive models, one relying on the transition probabilities governing the recent past, and another relying on natural sound statistics learned over a lifetime“ with “This result highlights the presence of an active predictive system that relies on natural sound statistics learned over a lifetime to process incoming auditory input”.

(2) Albeit the paradigm is well designed, I fail to see the grounding of the hypotheses laid by the authors as framed under the predictive coding perspective. The study assumes that responses to an omission at the beginning of a perceptual rhythmic pattern will be stronger than at the end. I feel this is unjustified. If anything, omission responses should be larger when the gap occurs at the end of the pattern, as that would be where stronger expectations are placed: if in my language a short sound occurs after a long one, and I perceptually group tone sequences of alternating tone duration accordingly, when I hear a short sound I will expect a long one following; but after a long one, I don't necessarily need to expect a short one, as something else might occur.

A similar point was advanced by Reviewer #1. We tried to clarify the rationale behind our hypothesis. Please refer to the response provided to the first comment of Reviewer #1 above.

(3) In this regard, it is my opinion that what is reflected in the data may be better accounted for (or at least, additionally) by a different neural response to an omission depending on the phase of an underlying attentional rhythm (in terms of Large and Jones rhythmic attention theory, for instance) and putative underlying entrained oscillatory neural activity (in terms of Lakatos' studies, for instance). Certainly, the fact that the aligned phase may differ depending on linguistic background is very interesting and would reflect the known behavioral effect.

We thank the Reviewer for this comment. We explored in more detail the possibility that the aligned phase may differ depending on linguistic background, which is indeed a very interesting hypothesis. In the phase analyses reported below we focused on the instantaneous phase angle time locked to the onset of short and long tones presented in the experiment.

In short, we extracted time intervals of two seconds centered on the onset of the tones for each participant (~200 trials per condition) and using a wavelet transform (implemented in Fieldtrip ft_freqanalysis) we targeted the 0.92 Hz frequency that corresponds to the rhythm of presentation of our pairs of tones. We extracted the phase angle for each time point and using the circular statistics toolbox implemented in Matlab we computed the Raleigh z scores across all the sensor space for each tone (long and short tone) and group (Spanish (Spa) dominants and Basque (Eus) dominants). This method evaluates the instantaneous phase clustering at a specific time point, thus evaluating the presence of a specific oscillatory pattern at the onset of the specific tone. 

Author response image 2.

Here we observe that the phase clustering was stronger in the right sensors for both groups. The critical point is to evaluate the phase angle (estimated in phase radians) for the two groups and the two tones and see if there are statistical differences. We focused first on the sensor with higher clustering (right temporal MEG1323) and observed very similar phase angles for the two groups both for long and short tones (see image below). We then focused on the four left fronto-temporal sensor pairs who showed the significant interaction: here we observed one sensor (MEG0412) with different effects for the two groups (interaction group by tone was significant, p=0.02): for short tones the “Watson (1961) approximation U2 test” showed a p-value of 0.11, while for long tones the p-value was 0.03 (after correction for multiple comparisons). 

Overall, the present findings suggest the tendency to phase aligning differently in the two groups to long and short tones in the left fronto-temporal hemisphere. However, the effect could be detected only in one gradiometer sensor and it was not statistically robust. The effect in the right hemisphere was statistically more robust, but it was not sensitive to group language dominance. 

Due to the inconclusive nature of these analyses regarding the role of language experience in shaping the phase alignment to rhythmic sound sequences, we prefer to keep these results in the public review rather than incorporating them in the article.  Nonetheless, we believe that this decision does not undermine the main finding that the group differences in the MMN amplitude are driven by long-term predictions – especially in light of the many studies indicating the MMN as a putative index of prediction error (e.g., Bendixen et al., 2012; Heilbron and Chait, 2018). Moreover, as suggested in the preliminary reply, despite evoked responses and oscillations are often considered distinct electrophysiological phenomena, current evidence suggests that these phenomena are interconnected (e.g., Studenova et al., 2023). In our view, the hypotheses that the MMN reflects differences in phase alignment and long-term prediction errors are not mutually exclusive.

Author response image 3.

(4) Source localization is performed on sensor-level significant data. The lack of  sourcelevel statistics weakens the conclusions that can be extracted. Furthermore, only the source reflecting the interaction pattern is taken into account in detail as supporting their hypotheses, overlooking other sources. Also, the right IFG source activity is not depicted, but looking at whole brain maps seems even stronger than the left. To sum up, source localization data, as informative as it could be, does not strongly support the author's claims in its current state. 

A similar comment was also advanced by Reviewer #1 (comment 2). We appreciate the suggestion to incorporate more comprehensive source analyses. In the new version of the paper, we perform new analyses on the source data using a new Atlas with more fine-grained parcellations of the ROIs, and focusing on peak activity to increase response’s sensitivity in space and time. We therefore invite the Reviewer to read the updated part on source reconstruction included in the Results and Methods sections of the paper. 

In the article, we report only the source reconstruction data from ROIs in the left hemisphere, because it is there that the interaction effect arises at the sensor level. However, we also explored the homologous regions in the right hemisphere, as requested by the Reviewer. A cluster-based permutation test focusing on the interaction between language group and omission type was performed on both the right STG and IFG data. No significant interaction emerged in any of these regions. Below a plot of the source activity time series over ROIs in the right STG and IFG. 

Author response image 4.

Reviewer #2 (Recommendations For The Authors):

In this set of private recommendations for the authors, I will outline a couple of minor comments and try to encourage additional data analyses that, in my opinion, would strengthen the evidence provided by the study. 

(1) As I noted in the public review, I believe an oscillatory analysis of the data would, on one hand, provide stronger support for the behavioral effect of rhythmic perceptual organization given the lack of behavioral direct evidence; and, on the other hand, provide evidence (to be discussed if so) for a role of entrained oscillation phase in explaining the different pattern of omission responses. One analysis the authors could try is to measure the phase angle of an oscillation, the frequency of which relates to the length of the binary pattern, at the onset of short and long tones, separately, and compare it across groups. Also, single trials of omission responses could be sorted according to that phase. 

Thanks for the suggestion. Please see phase analyses reported above.

(2) I wonder why source activity for the right IFG was not shown. I urge the authors to provide and discuss a more complete picture of the source activity found. Given the lack of source statistics (which could be performed), I find it a must to give an overall view. I find it so because I believe the distinction between perceptual grouping effects due to inherent acoustic differences across languages or semantic differences is so interesting. 

Thanks again for the invitation to provide a more complete picture of the source activity data. As mentioned in the response above, we invite the Reviewer to read the new related part included in the Results and Methods sections of the paper. In our updated source reconstruction analysis, we find that some regions around the left STG show a pattern that resembles the one found at the sensor-level, providing further support for the “acoustic” (rather than syntactic/semantic) nature of the effect. 

We did not report ROI analysis on the right hemisphere because the interaction effect at sensor level emerged on the left hemisphere. Yet, we included a summary of this analysis in the public response above. 

(3) Related to this, I have to acknowledge I had to read the whole Molnar et al. (2016) study to find the only evidence so far that, acoustically, in terms of sound duration, Basque and Spanish differ. This was hypothesized before but only at Molnar, an acoustic analysis is performed. I think this is key, and the authors should give it a deeper account in their manuscript. I spend my review of this study thinking, well, but when we speak we actually bind together different words and the syllabic structure does not need to reflect the written one, so maybe the effect is due to a high-level statistical prior related to the content of the words... but Molnar showed me that actually, acoustically, there's a difference in accent and duration: "Taken together, Experiments 1a and 1b show that Basque and Spanish exhibit the predicted differences in terms of the position of prosodic prominence in their phonological phrases (Basque: trochaic, Spanish: iambic), even though the acoustic realization of this prominence involves not only intensity in Basque but duration, as well. Spanish, as predicted, only uses duration as a cue to mark phrasal prosody." 

Thanks for the suggestion, the distinction in terms of sound duration in Spanish and Basque reported by Molnar is indeed very relevant for the current study. 

We add a few sentences to highlight the acoustic analysis by Molnar and the consequent acoustic nature of the reported effect.

In the introduction: “Specifically, the effect has been proposed to depend on the quasiperiodic alternation of short and long auditory events in the speech signal – reported in previous acoustic analyses (Molnar et al., 2016) – which reflect the linearization of function words (e.g., articles, prepositions) and content words (e.g., nouns, adjectives, verbs).”

In the discussion, paragraph 3, we changed “We hypothesized that this effect is linked to a long-term “duration prior” originating from the syntactic function-content word order of language, and specifically, from its acoustic consequences on the prosodic structure” with “We hypothesized that this effect is linked to a long-term “duration prior” originating from the acoustic properties of the two languages, specifically from the alternation of short and long auditory events in their prosody”.

In the discussion, end of paragraph eight: “The reconstruction of cortical sources associated with the omission of short and long tones in the two groups showed that an interaction effect mirroring the one at the sensor level was present in the left STG, but not in the left IFG (fig. 3, B, C, D). Pairwise comparisons within different ROIs of the left STG indicated that the interaction effect was stronger over primary (BA 41/42) rather than associative (BAs 22) portions of the auditory cortex. Overall, these results suggest that the “duration prior” is linked to the acoustic properties of a given language rather than its syntactic configurations”.

Now, some minor comments: 

(1) Where did the experiments take place? Were they in accordance with the Declaration of Helsinki? Did participants give informed consent? 

All the requested information has been added to the updated version of the manuscript. Thanks for pointing out this.

(2) The fixed interval should be called inter-stimulus interval. 

Thanks for pointing this out. We changed the wording as suggested.

(3) The authors state that "Omission responses allow to examine the presence of putative error signals decoupled from bottom-up sensory input, offering a critical test for predictive coding (Walsh et al 2020, Heilbron and Chait, 2018).". However the way omission responses are computed in their study is by subtracting the activity from the previous tone. This necessarily means that in the omission activity analyzed, there's bottom-up sensory input activity. As performing another experiment with a control condition in which a sequence of randomly presented tones with different durations to compare directly the omission activity in both sequences (experimental and control) is possibly too demanding, I at least urge the authors to incorporate the fact that their omission responses do reflect also tone activity. And consider, for future experiments, the inclusion of further control conditions. 

Thanks for the opportunity to clarify this aspect. Actually, the way we computed the omission MMN is not by subtracting the activity of the previous tone from the omission, but by subtracting the activity of randomly selected tones across the whole experiment. That is, we randomly selected around 120 long and short tones (i.e., about the same number as the omissions); we computed the ERF for the long and short tones; we subtracted these ERF from the ERF of the corresponding short and long omissions. We clarified these aspects in both the Materials and Methods (ERF analysis paragraph) and Results section.

Moreover, the subtraction strategy - which is the standard approach to calculate the MMN - allows to handle possible neural carryover effects arising from the perception of the tone preceding the omission.

The sentence "Omission responses allow to examine the presence of putative error signals decoupled from bottom-up sensory input, offering a critical test for predictive coding (Walsh et al 2020, Heilbron and Chait, 2018)." simply refer to the fact that the error responses resulting from an omission are purely endogenous, as omissions are just absence of an expected input (i.e., silence). On the other hand, when a predicted sequence of tones is disrupted by an auditory deviants (e.g., a tone with a different pitch or duration than the expected one), the resulting error response is not purely endogenous, but it partially includes the response to the acoustic properties of the deviant.

(4) When multiple clusters emerged from a comparison, only the most significant cluster was reported. Why? 

We found more than one significant cluster only in the comparison between pure omissions vs tones (figure 2 A, B). The additional significant cluster from this comparison is associated with a P-value of 0.04, emerges slightly earlier in time, and goes in the same direction as the cluster reported in the paper i.e., larger ERF responses for omission vs tones. We added a note specifying the presence of this second cluster, along with a figure on the supplementary material (Supplementary Fig. 1 A, B).

(5) Fig 2, if ERFs are baseline corrected -50 to 0ms, why do the plots show pre-stimulus amplitudes not centered at 0? 

This is because we combined the latitudinal and longitudinal gradiometers on the ERF obtained after baseline correction, by computing the root mean square of the signals at each sensor position (see also  https://www.fieldtriptoolbox.org/example/combineplanar_pipelineorder/). This information is reported in the methods part of the article.

(6) Fig 2, add units to color bars. 

Sure.

(7) Fig 2 F and G, put colorbar scale the same for all topographies. 

Sure, thanks for pointing this out.

(8) The interaction effect language (Spanish; Basque) X omission type (short; long) appears only in a small cluster of 4 sensors not located at the locations with larger amplitudes to omissions. Authors report it as left frontotemporal, but it seems to me frontocentral with a slight left lateralization.

(1) the fact that the cluster reflecting the interaction effect does not overlap with the peaks of activity is not surprising in our view. Many sources contribute to the generation of the MMN. The goal of our work was to establish whether there is also evidence for a long-term system (among the many) contributing to this. That is why we perform a first analysis on the whole omission response network (likely including many sources and predictive/attentional systems), and then we zoom in and focus on our hypothesized interaction. We never claim that the main source underlying the omissionMMM is the long-term predictive system. 

(2) The exact location of those sensors is at the periphery of the left-hemisphere omission response, which mainly reflects activity from the left temporal regions. The sensor location of this cluster could be influenced by multiple factors, including (i) the direction of the source dipoles determining an effect; (ii) the combination of multiple sources contributing to the activity measured at a specific sensor location, whose unmixing could be solved only with a beamforming source approach. Based on the whole evidence we collected also in the source analyzes we concluded that the major contributors to the sensor-level interaction are emerging from both frontal and temporal regions.

Reviewer #3 (Public Review):

(1) The main weaknesses are the strength of the effects and generalisability. The sample size is also relatively small by today's standards, with N=20 in each group. Furthermore, the crucial effects are all mostly in the .01>P<.05 range, such as the crucial interaction P=.03. It would be nice to see it replicated in the future, with more participants and other languages. It would also have been nice to see behavioural data that could be correlated with neural data to better understand the real-world consequences of the effect.

We appreciate the positive feedback from Reviewer #3. We agree that it would be nice to see this study replicated in the future with larger sample sizes and a behavioral counterpart. Below are a few comments concerning the weakness highlighted: 

(i) Concerning the sample size: a similar point was raised by Reviewer #1. We report our reply as presented above: “Despite a sample size of 20 participants per group can be considered relatively small for detecting an effect in a between-group design, it must be noted that our effect of interest was based on Molnar et al.’s (2016) experiment, where a sample size of 16 subjects per group was sufficient to detect the perceptual grouping effect. In Yoshida et al., 2010, the perceptual grouping effect arose with two groups of 20 7–8-month-old Japanese and English-learning infants. Based on these findings, we believe that a sample size of 20 participants per group can be considered appropriate for the current study”. We clarified these aspects in the new version of the manuscript.

(ii) We believe that the lack of behavioral data does not undermine the main findings of this study, given the careful selection of the participants and the well-known robustness of the perceptual grouping effect (e.g., Iversen 2008; Yoshida et al., 2010; Molnar et al. 2014; Molnar et al. 2016). As highlighted by Reviewer #2, having Spanish and Basque dominant “speakers as a sample equates that in Molnar et al. (2016), and thus overcomes the lack of direct behavioral evidence for a difference in rhythmic grouping across linguistic groups. Molnar et al. (2016)'s evidence on the behavioral effect is compelling, and the evidence on neural signatures provided by the present study aligns with it”. (iii) Regarding the fact that the “crucial effects are all mostly in the .01>P<.05 range”: we want to stress that the approach we used to detect the interaction effect was conservative, using a cluster-based permutation approach with no a priori assumptions about the location of the effect. The robustness of our approach has also been highlighted by Reviewer 2: “Data analyses. Sound, state-of-the-art methodology in the event-related field analyses at the sensor level.” In sum, despite some crucial effects being in the .01>P<.05 range, we believe that the statistical soundness of our analysis, combined with the lack of effect in the control condition, provides compelling evidence for our H1.

Reviewer #3 (Recommendations For The Authors):

Figures - Recommend converting all diagrams and plots to vector images to ensure they remain clear when zoomed in the PDF format. 

Sure, thanks. 

Figure 1: To improve clarity, the representation of sound durations in panels C and D should be revisited. The use of quavers/eighth notes can be confusing for those familiar with musical notation, as they imply isochrony. If printed in black and white, colour distinctions may be lost, making it difficult to discern the different durations. A more universal representation, such as spectrograms, might be more effective. 

Thanks for the suggestion. It’s true that the quavers/eighth notes might be confusing in that respect. However, we find this notation as a relatively standard approach to define paradigms in auditory neuroscience, see for instance the two papers below. In the new version of the manuscript, we specified in the captions under the figure that the notes refer to individual tones, in order to avoid ambiguities.

- Wacongne, C., Labyt, E., Van Wassenhove, V., Bekinschtein, T., Naccache, L., & Dehaene, S. (2011). Evidence for a hierarchy of predictions and prediction errors in human cortex. Proceedings of the National Academy of Sciences, 108(51), 20754-20759.

- Dehaene, S., Meyniel, F., Wacongne, C., Wang, L., & Pallier, C. (2015). The neural representation of sequences: from transition probabilities to algebraic patterns and linguistic trees. Neuron, 88(1), 2-19.

Figure 2 : In panel C of Figure 2, please include the exact p-value for the interaction observed. Refrain from using asterisks or "n.s." and opt for exact p-values throughout for the sake of clarity. 

Thank you for your suggestion. We have included the exact p-value for the interaction in panel C of Figure 2. However, for the remaining figures, we have chosen to maintain the use of asterisks and "n.s.". We would like our pictures to convey the key findings concisely, while the numerical details can be found in the article text. The caption below the image also provides guidance on the interpretation of the p-values: (statistical significance: **p < 0.01, *p < 0.05, and ns p > 0.05).  

Figure 3 Note typo "Omission reponse"

Fixed. Thanks for noticing the typo. 

A note: we moved the figure reflecting the main effect of long tone omission and the lack of main effect of language background (Figure 4 in the previous manuscript) in the supplementary material (Supplementary Figure 2).

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