Author response:

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

In response to Reviewer #2, we agree with the reviewer that it needs to be noted that not all forms of recognition are the same and have added the following: "However, we note that not all forms of recognition are the same; researchers may prefer to have their work featured instead of personal stories or critiques of the scientific environment."

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

We thank both reviewers for their detailed comments and insightful suggestions. Below we summarize our responses to each concern in addition to the edits within the manuscript.

We would also like to add a clarification to the eLife assessment, it states “This important bibliometric analysis shows that authors of scientific papers whose names suggest they are female or East Asian get quoted less often in news stories about their work.” We show that individuals with names predicted to be from women or East Asian name origins are less likely to be quoted or mentioned in Nature’s scientific news stories than expected by publication demographics. In this study, we did not compare the level of coverage of a scientific article by the demographics of the authors of the article.

Reviewer #1

The article is not so clearly structured, which makes it hard to follow. A better framing, contextualization, and conceptualization of their analysis would help the readers to better understand the results. There are some unclear definitions and wrong wording of key concepts.

We have adapted our wording in the text and added a more detailed discussion which hopefully makes the paper easier to comprehend. These changes are described in the context of your reviewer's suggestions and addressed in the next section.

Language use: Male/Female refers to sex, not to gender.

We have now updated the language throughout the text. Thank you for pointing this out.

Regional disparities are not the same as names' origin. While the first might relate to the academic origin of authors, inferred from their institutional belonging, the latter reflects the authors' inferred identity. Ethnic identities and the construction of prejudice against specific populations need proper contextualization.

We have added better contextualization in the manuscript and reworded the section in our results and discussion to clarify that we are analyzing disparities related to perceived ethnicity and not regions. We also added the following text to the results section “In our analysis, we use name origin as an estimate for the perceived ethnicity of a primary source by a journalist. Our prediction is not intended to assign ethnicity to an individual, but to be used broadly as a tool to quantify representational differences in a journalist's sociologically constructed perception of a primary source's ethnicity.” We also added the following text to our Discussion: “Our use of name origins is a proxy for a journalist's or referring scholarly peer’s potential perceptions of the ethnicity of a primary source as signaled by an individual's name. We do not intend to assign an identity to an individual, but to generate a broad metric to measure possible bias for particular ethnicities during journalists' primary source gathering.”

It would be helpful to have a clear definition of what are quotes, mentions, and citations. For me, it was not so clear and made understanding the results more difficult.

We added the following text to the results section Extracted Data Used for Analysis: “Quoted names are any names that were attached to a quote within the article. Mentioned names are any names that were stated within the article. Cited names are all author names of a scientific paper that was cited in the news article.”

The comparison against Nature published research articles is not perfect because journalists will also cover articles not published in Nature. If for example, the gender representation in the quoted articles is not the same between Nature journals and other journals, then this source of inequality would be missing (e.g. if the journalists are biased against women, but not as much when they published in Nature, because they are also biased towards Nature articles). Also, the gender representation among Nature authors could not be the same as in general. Nevertheless, this seems to be a fair benchmark, especially if the authors did not have access to other more comprehensive databases. But a statement of limitations including these potential issues would be good to have.

To add better context to the generalizability of our work, we added the following text to our discussion: “Furthermore, the news articles present on "www.nature.com" are intended for a very specific readership that may not be reflective of more broad scientific news outlets. In a separate analysis, we took a cursory look into a comparison with The Guardian and found similar disparities in gender and name origin. However, it is not clear which publications should be used as a comparator for science-related articles in The Guardian, and difficult to compare relative rates of representation. While other science news outlets may not have a direct comparator, it would be useful to take a broad comparison across multiple science news outlets to compare against one another. Our existing pipeline could be easily applied to other science news outlets and identify if there exists a consistent pattern of disparity regardless of the intended readership.”

"we select the highest probability origin for each name as the resultant assignment". Threshold based approaches for race/ethnicity name-based inference have been criticized by the literature as they might reproduce biases (see Kozlowski, D., Murray, D. S., Bell, A., Hulsey, W., Larivière, V., Monroe-White, T., & Sugimoto, C. R. (2022). Avoiding bias when inferring race using name-based approaches. Plos one, 17(3), e0264270.). The authors could use the full distribution of probabilities over names instead of selecting one. The formulae proposed (3-5) could be easily adapted to this change.

We thank the author for pointing this out. We have updated our analysis to use the probabilities instead of hard assignments. Figure 3 and formulae 3-5 have been updated. While we observe a slight shift in the calculated values, the overall trends are unchanged.

Is it possible to make an analysis that intersects both name origin and gender? I am not sure if the sample size would allow for this, but if some other dimensions were collapsed, it would be very important to show what happens at the intersection of these two dimensions of discrimination.

We agree that identifying any differences in quotation patterns at the intersection of gender and name origin would be very useful to identify. To address this, we added supplemental table 5. This table identifies the number of quotes per predicted name origin and gender over all years and article types. In this table, we don’t see a significant difference in gender distribution across predicted name origins.

Given a larger sample size, we would be able to better identify more subtle differences, but at this sample size, we cannot make more detailed inferences. Additionally, this also addresses a QC-issue, where predicted gender accuracy varies by name origin, specifically East Asian name origin. From our data, we don’t see a large difference in proportions across any name origin. We added the following text to the results section to incorporate this analysis:

“However, it should be noted that the error rate varies by name origin with the largest decrease in performance on names with an Asian origin [@doi:10.7717/peerj-cs.156;@doi:10.5195/jmla.2021.1252]

. In our analysis, we did not observe a large difference in names predicted to come from a man or woman between predicted East Asian and other name origins (Table 5). “

The use of vocabulary should be more homogeneous. For example, in page 13 the authors start to use the concepts of over/under enrichment, which appeared before in a title but was not used.

The text has been updated to remove all mentions of “over/under enrichment” with “over/under representation”

In the discussions section, it would be important to see as a statement of limitations the problems that automatic origin and gender inference have.

We thank the reviewer for this suggestion. We have added the following paragraph to our discussion.

Computational tools enabled us to automatically analyze thousands of articles to identify existing disparities by gender and name origin, but these tools are not without limitations. Our tools are unable to identify non-binary people and rely on gender predictors that are known to have region-specific biases, with the largest decrease in performance on names of an Asian origin [@doi:10.7717/peerj-cs.156;@doi:10.5195/jmla.2021.1252]. Furthermore, name origin is only a proxy for externally perceived racial or ethnic origins of a source or author and is not as accurate as self-identified race or ethnicity. Self-identification better captures the lived experience of an individual that computational estimates from a name can not capture. This is highlighted in our inability to distinguish between Black and White people from the US by their names. As the collection of demographic data by publication outlets grows, we believe this will enable a more fine-grained and accurate analysis of disparities in scientific journalism.

Figures 2a and 3a show that the affiliations of authors and their countries was going to be used in this analysis. Yet, this section is not present in the article. I would encourage the authors to add this to the analysis as it would show important patterns, and to intersect the dimensions of gender, name origin and country.

We were interested in using this analysis in our work, but unfortunately the sample size of cited works in each country was too small to make inferences. If this work was extended to larger scientific outlets to include larger corpora such as The Guardian or New York Times, we think one could be able to make more robust inferences. Since our work only focuses on Nature, we decided not to include this analysis. However, we do include a section in our discussion for future work.

“As a proxy for measuring possible geographical bias of a journalist, we attempted to identify if there was any geographical bias of cited authors. To do this, we identified the affiliation of each cited author and identified their affiliated country. Unfortunately, we could not robustly extract a large enough number of cited authors from different countries to make any conclusive statements. Expanding our work to other science journalism outlets could help identify possible ways in which geographic region, genders, and perceived ethnicity interact and affect scientific visibility of specific groups. While we are unable to identify that journalists have a specific geographical bias, having reporters explicitly focused on specific regional sources will broaden coverage of international opinions in science.”

It is not clear at that point what column dependence means.

The abstract has been updated to state, “Gender disparity in Nature quotes was dependent on the article type.”

Reviewer #2

We thank the reviewer for their very detailed and insightful suggestions regarding our analysis and the key caveats that needed better contextualization in our analysis. We went through each major point the reviewer brought up below and included any additional text that was needed.

In some cases, the manuscript lacks consistency in terminology, and uses word choice that is strange (e.g., "enrichment" and "depletion" when discussion representation).

We thank the review for pointing this out, we have removed all instances of depletion/enrichment for over/under-representation

Caveats to Claim 1. So while Claim 1 holds, it does not hold for all comparator sets and for all years. I don't think this is critical of the paper-the authors do discuss the trend in Claim 2-but interpretation of this claim should take care of these caveats, and readers should consider the important differences in first and last authorship.

We thank the reviewer for their detailed feedback on this section. We have added the missing contextualization of our results. In the results section, I changed the figure caption to: “Speakers predicted to be men are sometimes overrepresented in quotes, but this depends on the year and article type.” Added the following paragraph “When considering the relative proportion of authors and speakers predicted to be men, we only find a slight over-representation of men. This overrepresentation is dependent on the authorship position and the year. Before 2010, quotes predicted as from men are overrepresented in comparison to both first and last authors, but between 2010 and 2017 quotes predicted from men are only overrepresented in comparison for first authors. In 2020, we find a slight over-representation of quotes predicted to be from women relative to first and last authors, but still severely under-represented when considering the general population. The choice of comparison between first and last authors can reveal different aspects of the current state of academia. While this does not hold in all scientific fields, first authors are typically early career scientists and last authors are more senior scientists. It has also been shown that early career scientists tend to be more diverse than senior scientists [@doi:10.7554/eLife.60829; @doi:10.1096/fj.201800639]. Since we find that quotes are only slightly more likely to come from a last author, it is reasonable to compare the relative rate of predicted quotes from men to either authorship position. Comparison with last authorships may reveal more how gender bias currently exists whereas comparison with early career scientists may reveal bias in comparison to a future, more possibly diverse academic environment. We hope that increased representation and recognition of women in science, even beyond what is observed in authorship, can increase the proportion of women first and last authors such that it better reflects the general population.”

Generalizability to other contexts of science journalism:

We thank the reviewer for their feedback on the generalizability of our work. We have now added the following text to our discussion to provide the reader with a better context of our results: “To articles presented on "www.nature.com" are intended for a very specific readership that may not be reflective of more broad scientific news outlets. In a separate analysis, we took a cursory look into a comparison with The Guardian and found very similar disparities in gender and name origin. However, it is not clear which publications should be used as a comparator for science-related articles in The

Guardian, and difficult to compare relative rates of representation. While other science news outlets may not have a direct comparator, it would be useful to take a broad comparison across multiple science news outlets to compare against one another. Our existing pipeline could be easily applied to other science news outlets and identify if there exists a consistent pattern of disparity regardless of the intended readership. ”

Shallow discussion:

The authors highlight gender parity in career features, but why exactly is there gender parity in this format

We thank the reviewer for encouraging us to better contextualize our findings in the broader discourse. We have now added several sections to our Discussion. To address gender parity, we have added the following text: “This finding, coupled with the near equal number of articles written by journalists predicted to be men or women, argues for more diversity in topical coverage. "Career Feature" articles highlight current topics relevant to working scientists and frequently highlight systemic issues with the scientific environment. This column allows space for marginalized people to critique the current state of affairs in science or share their personal stories. This type of content encourages the journalist to seek out a diverse set of primary sources. Including more content that is not primarily focused on recent publications, but all topics surrounding the practice of science, can serve as an additional tool to rapidly achieve gender parity in journalistic recognition.”

Representation in quotations varies by first and last author, most certainly as a result of the academic division of labor in the life sciences. However, what does it say about the scientific quotation that it appears first authors are more often to be quoted? Does this mean that the division of labor is changing such that the first authors are the lead scientists? Or does it imply that senior authors are being skipped over, or giving away their chance to comment on a study to the first author?

We thank the reviewer for asking bringing up these important questions. We have added better context to our first author analysis in our discussion. We have included the following two sections to address this. Also, we want to state that we find last authors to be slightly more quoted than first authors, as depicted in Fig. 2d., with first author quotation percentage largely appearing below the red line. We included this text in a response above and include it again here for convenience.

“Before 2010, quotes predicted as from men are overrepresented in comparison to both first and last authors, but between 2010 and 2017 quotes predicted from men are only overrepresented in comparison for first authors. In 2020, we find a slight over-representation of quotes predicted to be from women relative to first and last authors, but still severely under-represented when considering the general population. The choice of comparison between first and last authors can reveal different aspects of the current state of academia. While this does not hold in all scientific fields, first authors are typically early career scientists and last authors are more senior scientists. It has also been shown that early career scientists tend to be more diverse than senior scientists [@doi:10.7554/eLife.60829; @doi:10.1096/fj.201800639]. Since we find that quotes are only slightly more likely to come from a last author, it is reasonable to compare the relative rate of predicted quotes from men to either authorship position. Comparison with last authorships may reveal more how gender bias currently exists whereas comparison with early career scientists may reveal bias in comparison to a future, more possibly diverse academic environment. We hope that increased representation and recognition of women in science, even beyond what is observed in authorship, can increase the proportion of women first and last authors such that it better reflects the general population.”

“In our analysis, we also find that there are more first authors with predicted East Asian name origin than last authors. This is in contrast to predicted Celtic/English and European name origins.

Furthermore, we see that the amount of first author people with predicted East Asian name origins is increasing at a much faster rate than quotes are increasing. If this mismatched rate of representation continues, this could lead to an increasingly large erasure of early career scientists with East Asian name origins. As noted before, focusing on increasing engagement with early career scientists can help to reduce the growing disparity of public visibility of scientists with East Asian name origins.”

What might be the downstream impacts on the public stemming from the under-representation of scientists with East Asian names? According to Figure 3d, not only are East Asian names under-represented in quotations, but they are becoming more under-represented over time as they appear as authors in a greater number of Nature publications; Those with European names are proportionately represented in quotations given their share of authors in Nature. Why might this be, especially seeing as Anglo names are heavily over-represented?

To address this point, we have added the following text to our discussion: “In our analysis, we also find that there are more first authors with predicted East Asian name origin than last authors. This is in contrast to predicted Celtic/English and European name origins. Furthermore, the amount of first author people with predicted East Asian name origins is increasing at a much faster rate than quotes are increasing. If this mismatched rate of representation continues, this could lead to an increasingly large erasure of early career scientists with East Asian name origins. As noted before, focusing on increasing engagement with early career scientists can help to reduce the growing disparity of public visibility of scientists with East Asian name origins.”

I am very confused by Figure 1B. It mixes the counts of News-related items with (non-Springer) research articles in a single stacked bar plot which makes determining the quantity of either difficult. I would advise splitting them out

Figure 1B has been updated, and the News and Research articles have been separated.

When querying the first 2000 or so results from the SpringerNature API, are the authors certain that they are getting a random sample of papers?

These papers were the first 200 English language "Journal" papers returned by the Springer Nature API for each month, resulting in 2400 papers per year from 2005 through 2020. These papers are the first 200 papers published each month by a Springer Nature journal, which may not be completely random, but we believe to be a reasonably representative sample. Furthermore, the Springer Nature comparator set is being used as an additional comparator to the complete set of all Nature research papers used in our analyses.

In all figures: the authors use capital letters to indicate panels in the caption, but lowercase letters in the figure itself and in the main text. This should be made consistent.

This has been updated.

In all figures: the authors should make the caption letter bold in the figure captions, which makes it much easier to find descriptions of specific panels

This has been updated.

In the section "coreNLP": the authors mention "co-reference resolution" but without really remarking why it is being used. This is an issue throughout the methods-the authors describe what method they are using but either they don't mention why they are using that method until later, or else not at all.

We have added better reasoning behind our coreNLP selected methods: “We used the standard set of annotaters: tokenize, ssplit, pos, lemma, ner, parse, coref, and additionally the quote annotator. These perform text tokenization, sentence splitting, part of speech recognition, lemmatization, named entity recoginition, division of sentences into constituent phrases, co-reference resolution, and identification of quoted entities, respectively. We used the "statistical" algorithm to perform coreference resolution for speed. Each of these aspects is required to identify the names of quoted or mentioned speakers and identify any of their associated pronouns. All results were output to json format for further downstream processing.”

We included a better description of scrapy: “Scrapy is a tool that applies user-defined rules to follow hyperlinks on webpages and return the information contained on each webpage.

We used Scrapy to extract all web pages containing news articles and extract the text.”

We also included our motivation for bootstrapping: “We used the boostrap method to construct confidence intervals for each of our calculated statistics.”

In the section "Name Formatting for Gender Prediction in Quotes or Mentions", genderizeR is mentioned before an introduction to the tool

We added the following text to provide context: “Even though genderizeR, the computational method used to predict the name's gender, only uses the first name to make the gender prediction, identifying the full name gives us greater confidence that we correctly identified the first name. “

In the section "Name Formatting for Gender Prediction of Authors", you state that you exclude papers with only one author. How many papers is this? I assume few, in Nature, but if not I can imagine gender differences based on who writes first-authored papers.

We find that the number excluded is roughly 7% of all papers, which is consistent across Nature and Springer Nature (1113/15013 for cited springer articles, 2899/42155 for random springer articles, 955/12459 for nature authors). We have added the following text to the manuscript for better context: “Roughly 7% of all papers were estimated to be by a single author and removed from this analysis.: 1113/15013 for cited Springer articles, 2899/42155 for random Springer articles, 955/12459 for Nature research articles.”

In "Name Origin Analysis", for the in-text reference to Equation 3: include the prefix "Eq." or similar to mark this as referencing the equation and not something else

This has been updated.

The use of the word "enrichment" in reference to the representation of East Asian authors is strange and does not fit the colloquial definition of the term. I suggest just using a simpler term like "representation" instead

Similarly, the authors use the word "depletion" to reflect the lower rate of quotes to scientists with East-Asian names, but I feel a simpler word would be more appropriate.

We thank the reviewer for this suggestion, all instances of “enrichment/depletion” have been replaced with “over/under representation”

The authors claim in Figure 2d that there is a steady increase in the rate of first author citations, however, this graph is not convincing. It appears to show much more noise than anything resembling a steady change.

We have reworded our figure description to state that there is a consistent bias towards quoting last authors. Our figure description now states: “Panel d shows a consistent but slight bias towards quoting the last author of a cited article than the first author over time.”

Supplemental Figures 1b and 1c do not seem to be mentioned in the main text, and I struggle to see their relevance.

We thank the reviewer for identifying this error; these subpanels have been removed.

Author response:

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

Point-by-point response to concerns raised by reviewer #3:

The manuscript has improved very substantially in revision. The authors have clearly taken the comments on board in good faith. Yet, some small concerns remain around the behavioural analysis.

In Fig. 8H and H' average sleep/day is ~100. Is this minutes of sleep? 100 min/day is far too low, is it a typo?

The numbers for sleep bouts are also too low to me e.g. in Fig 9 number of sleep bouts avg around 4.

In their response to reviewers the authors say these errors were fixed, yet the figures appear not to have been changed. Perhaps the old figures were left in inadvertently?

Indeed this correction was somehow missed and we thank the reviewer for noticing this. We have now corrected Fig 8H-H’ and Fig 9D.  

The circadian anticipatory activity analyses could also be improved. The standard in the field is to perform eduction analyses and quantify anticipatory activity e.g. using the method of Harrisingh et al. (PMID: 18003827). This typically computed as the ratio of activity in the 3hrs preceding light transition to activity in the 6hrs preceding light transition.

In their response to reviewers, the authors have revised their anticipation analyses by quantifying the mean activity in the 6 hrs preceding light transition. However, in the method of Harrisingh et al., anticipation is the ratio of activity in the 3hrs preceding light transition to activity in the 6hrs preceding light transition. Simply computing the activity in the 6hrs preceding light transition does not give a measure of anticipation, determining the ratio is key.

We acknowledge the importance of obtaining accurate results in our analysis, therefore we have re-evaluated the anticipation activity by measuring the ratio of the mean activity in the 3h preceding light transition over the activity in the 6h preceding light transition. We have reported the data as percentages in Fig 8F-G and modified the figure legends accordingly.

Author response:

eLife assessment 

This important study provides evidence for a combination of the latest generation of Oxford Nanopore Technology long reads with state-of-the art variant callers enabling bacterial variant discovery at accuracy that matches or exceeds the current "gold standard" with short reads. The evidence supporting the claims of the authors is convincing, although the inclusion of a larger number of reference genomes would further strengthen the study. The work will be of interest to anyone performing sequencing for outbreak investigations, bacterial epidemiology, or similar studies. 

We thank the editor and reviewers for the accurate summary and positive assessment. We address the comment about increasing the number of reference genomes in the response to reviewer 2.

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

The authors assess the accuracy of short variant calling (SNPs and indels) in bacterial genomes using Oxford Nanopore reads generated on R10.4 flow cells from a very similar genome (99.5% ANI), examining the impact of variant caller choice (three traditional variant callers: bcftools, freebayes, and longshot, and three deep learning based variant callers: clair3, deep variant, and nano caller), base calling model (fast, hac and sup) and read depth (using both simplex and duplex reads). 

Strengths: 

Given the stated goal (analysis of variant calling for reads drawn from genomes very similar to the reference), the analysis is largely complete and results are compelling. The authors make the code and data used in their analysis available for re-use using current best practices (a computational workflow and data archived in INSDC databases or Zenodo as appropriate). 

Weaknesses: 

While the medaka variant caller is now deprecated for diploid calling, it is still widely used for haploid variant calling and should at least be mentioned (even if the mention is only to explain its exclusion from the analysis). 

We agree that this would be an informative addition to the study and will add it to the benchmarking.

Appraisal: 

The experiments the authors engaged in are well structured and the results are convincing. I expect that these results will be incorporated into "best practice" bacterial variant calling workflows in the future. 

Thank you for the positive appraisal.

Reviewer #2 (Public Review): 

Summary: 

Hall et al describe the superiority of ONT sequencing and deep learning-based variant callers to deliver higher SNP and Indel accuracy compared to previous gold-standard Illumina short-read sequencing. Furthermore, they provide recommendations for read sequencing depth and computational requirements when performing variant calling. 

Strengths: 

The study describes compelling data showing ONT superiority when using deep learning-based variant callers, such as Clair3, compared to Illumina sequencing. This challenges the paradigm that Illumina sequencing is the gold standard for variant calling in bacterial genomes. The authors provide evidence that homopolymeric regions, a systematic and problematic issue with ONT data, are no longer a concern in ONT sequencing. 

Weaknesses: 

(1) The inclusion of a larger number of reference genomes would have strengthened the study to accommodate larger variability (a limitation mentioned by the authors). 

Our strategic selection of 14 genomes—spanning a variety of bacterial genera and species, diverse GC content, and both gram-negative and gram-positive species (including M. tuberculosis, which is neither)—was designed to robustly address potential variability in our results. Moreover, all our genome assemblies underwent rigorous manual inspection as the quality of the true genome sequences is the foundation this research is built upon. Given this, the fundamental conclusions regarding the accuracy of variant calls would likely remain unchanged with the addition of more genomes.  However, we do acknowledge that a substantially larger sample size, which is beyond the scope of this study, would enable more fine-grained analysis of species differences in error rates.

(2) In Figure 2, there are clearly one or two samples that perform worse than others in all combinations (are always below the box plots). No information about species-specific variant calls is provided by the authors but one would like to know if those are recurrently associated with one or two species. Species-specific recommendations could also help the scientific community to choose the best sequencing/variant calling approaches.

Thank you for highlighting this observation. The precision, recall, and F1 scores for each sample and condition can be found in Supplementary Table S4. We will investigate the samples that consistently perform below expectation to determine if this is associated with specific species, which may necessitate tailored recommendations for those species. Additionally, we will produce a species-segregated version of Figure 2 for a clearer interpretation and will place it in the supplementary materials.

(3) The authors support that a read depth of 10x is sufficient to achieve variant calls that match or exceed Illumina sequencing. However, the standard here should be the optimal discriminatory power for clinical and public health utility (namely outbreak analysis). In such scenarios, the highest discriminatory power is always desirable and as such an F1 score, Recall and Precision that is as close to 100% as possible should be maintained (which changes the minimum read sequencing depth to at least 25x, which is the inflection point).

We agree that the highest discriminatory power is always desirable for clinical or public health applications. In which case, 25x is probably a better minimum recommendation. However, we are also aware that there are resource-limited settings where parity with Illumina is sufficient. In these cases, 10x depth from ONT would provide sufficient data.

The manuscript currently emphasises the latter scenario, but we will revise the text to clearly recommend 25x depth as a conservative aim in settings where resources are not a constraint, ensuring the highest possible discriminatory power for applications like outbreak analysis.

(4) The sequencing of the samples was not performed with the same Illumina and ONT method/equipment, which could have introduced specific equipment/preparation artefacts that were not considered in the study. See for example https://academic.oup.com/nargab/article/3/1/lqab019/6193612. 

To our knowledge, there is no evidence that sequencing on different ONT machines or barcoding kits leads to a difference in read characteristics or accuracy. To ensure consistency and minimise potential variability, we used the same ONT flowcells for all samples and performed basecalling on the same Nvidia A100 GPU. We will update the methods to emphasise this.

For Illumina and ONT, the exact machines used for which samples will be added as a supplementary table. We will also add a comment about possible Illumina error rate differences in the ‘Limitations’ section of the Discussion.

In summary, while there may be specific equipment or preparation artifacts to consider, we took steps to minimise these effects and maintain consistency across our sequencing methods.

Reviewer #3 (Public Review): 

Hall et al. benchmarked different variant calling methods on Nanopore reads of bacterial samples and compared the performance of Nanopore to short reads produced with Illumina sequencing. To establish a common ground for comparison, the authors first generated a variant truth set for each sample and then projected this set to the reference sequence of the sample to obtain a mutated reference. Subsequently, Hall et al. called SNPs and small indels using commonly used deep learning and conventional variant callers and compared the precision and accuracy from reads produced with simplex and duplex Nanopore sequencing to Illumina data. The authors did not investigate large structural variation, which is a major limitation of the current manuscript. It will be very interesting to see a follow-up study covering this much more challenging type of variation. 

We fully agree that investigating structural variations (SVs) would be a very interesting and important follow-up. Identifying and generating ground truth SVs is a nontrivial task and we feel it deserves its own space and study. We hope to explore this in the future.

In their comprehensive comparison of SNPs and small indels, the authors observed superior performance of deep learning over conventional variant callers when Nanopore reads were basecalled with the most accurate (but also computationally very expensive) model, even exceeding Illumina in some cases. Not surprisingly, Nanopore underperformed compared to Illumina when basecalled with the fastest (but computationally much less demanding) method with the lowest accuracy. The authors then investigated the surprisingly higher performance of Nanopore data in some cases and identified lower recall with Illumina short read data, particularly from repetitive regions and regions with high variant density, as the driver. Combining the most accurate Nanopore basecalling method with a deep learning variant caller resulted in low error rates in homopolymer regions, similar to Illumina data. This is remarkable, as homopolymer regions are (or, were) traditionally challenging for Nanopore sequencing. 

Lastly, Hall et al. provided useful information on the required Nanopore read depth, which is surprisingly low, and the computational resources for variant calling with deep learning callers. With that, the authors established a new state-of-the-art for Nanopore-only variant, calling on bacterial sequencing data. Most likely these findings will be transferred to other organisms as well or at least provide a proof-of-concept that can be built upon. 

As the authors mention multiple times throughout the manuscript, Nanopore can provide sequencing data in nearly real-time and in remote regions, therefore opening up a ton of new possibilities, for example for infectious disease surveillance. 

However, the high-performing variant calling method as established in this study requires the computationally very expensive sup and/or duplex Nanopore basecalling, whereas the least computationally demanding method underperforms. Here, the manuscript would greatly benefit from extending the last section on computational requirements, as the authors determine the resources for the variant calling but do not cover the entire picture. This could even be misleading for less experienced researchers who want to perform bacterial sequencing at high performance but with low resources. The authors mention it in the discussion but do not make clear enough that the described computational resources are probably largely insufficient to perform the high-accuracy basecalling required. 

We have provided runtime benchmarks for basecalling in Supplementary Figure S16 and detailed these times in Supplementary Table S7. In addition, we state in the Results section (P10 L228-230) “Though we do note that if the person performing the variant calling has received the raw (pod5) ONT data, basecalling also needs to be accounted for, as depending on how much sequencing was done, this step can also be resource-intensive.”

Even with super-accuracy basecalling considered, our analysis shows that variant calling remains the most resource-intensive step for Clair3, DeepVariant, FreeBayes, and NanoCaller. Therefore, the statement “the described computational resources are probably largely insufficient to perform the high-accuracy basecalling required”, is incorrect. However, we will endeavour to make the basecalling component and considerations more prominent in the Results and Discussion.

Author response:

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

Reviewer #1 (Recommendations For The Authors):

(1) The modeling process is outlined, but an explanation of why Maxent (Phillips & Dudík, 2008) was chosen for SDMs and why the specified predictor variables were used could provide additional context. This clarity would help readers understand the rationale behind the methodology.

In L.558-571 (Predictor variables subsection), we added the explanation about predictor variables as follows:

“Predictors encompass a range of environmental variables recognized to impact species distribution (Table 3): land use (Newbold et al., 2015), climate (bioclim variables (Booth et al., 2014)), vegetation (Abe, 2018), lithology (Ott, 2020) and elevational range (Udy et al., 2021). Additionally, categorical variables representing known biogeographic regions, reflecting geological history, were included. We applied  Blakiston's Line —Tsugaru straits dividing the northern and main islands of Japan (i.e., Hokkaido and Honshu islands)— reflecting a significant historical migration barrier for mammals and birds (Dobson, 1994; Saitoh et al., 2015). Due to the distinct fauna (Wepfer et al., 2016; Yamasaki, 2017), we also specified oceanic islands (i.e. Ogasawara and Daito isles) which have never been connected with the Asiatic continents. Continuous environmental variables were transformed into linear, quadratic and hinge feature classes to illustrate nonlinear associations between environments and species occurrence (Phillips et al., 2017). The regularisation multiplier was set at 2.5, falling within the established optimal range of 1.5 to 4 (Elith et al., 2010; MorenoAmat et al., 2015).”

In L.614-618 (Modelling subsection), we explain why we chose MaxEnt:

“To model species distributions from presence-only data, several algorithms have been utilised, including generalised additive models, random forest, and neural networks (Norberg et al., 2019; Valavi et al., 2022). In our study, we opted for MaxEnt (Phillips and Dudík, 2008) due to its high estimation accuracy and relatively low computational burden (Valavi et al., 2022).”

(2) While the study outlines a manual reidentification process by experts for wild individuals, it might be beneficial to elaborate on the criteria or expertise level of these experts. This transparency ensures the reliability of the reidentification process. Reply

In L.519-523, we added description about experts as follows:

“These experts have professional backgrounds, serving as a technician at a prefectural research institute (fish), highly-experienced field survey conductors (plants and insects, respectively), a post-doctoral researchers (amphibians and reptiles, and mammals, respectively), and a museum curator (mollusks) specialising in the focal taxa.”

(3) The analysis of the effects of data type (Biome+Traditional data or Traditional survey data) on BI is comprehensive. However, a brief discussion on the potential implications of these effects on the study's overall conclusions could add depth to the interpretation.

We enforced our discussion about the causes and consequences of improved modelling accuracy. 

In L.276-282, we argued about the causes: 

“Therefore, incorporating Biome data could significantly enhance modelling accuracy in urban and suburban landscapes, which are typically underrepresented in traditional survey data. As pseudo-absences are selected based on search effort, our models utilise numerous pseudoabsences from these areas. Consequently, this might lead to better estimation of species absence in such areas, not just presence, resulting in an overall increase in model accuracy across a wider range of species.”  

In L.370-387, we argued how improved modelling accuracy may help build naturepositive society as follows:

“By blending data from traditional surveys and communities, we improved the accuracy of species distribution estimates. This enhanced estimation lays the groundwork for more precise subsequent analyses. For instance, estimated distributions will be useful in selecting new protected areas or areas with OECMs (Other Effective area-based Conservation Measures: allowing a wider range of land use as long as biodiversity and ecosystem services are sustained/improved). Using estimated distributions of each species, hotspots of species or evolutionary diverse taxa can be inferred. Such sites will be good candidates for protected areas (Jones et al., 2016) or OECMs (Shiono et al., 2021). Further, estimated distributions can be used as input for spatial conservation prioritisation tools (e.g. Marxan (Ball et al., 2009)). 

In our experience, stakeholders—including corporate social responsibility managers and conservation practitioners—often seek the list of species potentially inhabiting their locations. Due to the uncertainty of SDMs and their thresholding into presence/absence, on-site surveys remain essential for assessing biodiversity status. SDMs can make such surveys costeffective by screening important locations for on-site assessment (e.g., Locate phase in TNFD framework) and narrowing down the target species for surveying. Improved estimation through SDMs can mitigate risks associated with their use in society and enable more informed decisionmaking for conservation efforts.”

Following the editorial policy, we have reorganised our supplementary materials as follows:

-        Formerly Supplementary File 1 - Remains unchanged.

-        Formerly Supplementary File 2 - Transferred into the main text, in the subsection "Filtering suspicious occurrence record in Biome data" in the Methods section, and Table 2. Citations remain as Supplementary File 2.

-        Formerly Supplementary File 3 - Remains unchanged.

-        Formerly Supplementary File 4 - Transferred into "Figure 3—figure supplement 1".

-        Formerly Supplementary File 5 - Transferred into Figure 4.

-        Formerly Supplementary File 6 - Transferred into the main text, in the subsection "Predictor variables" in the Methods section and Table 3.

-        Formerly Supplementary File 7 - Transferred into the main text, in the subsection "Pseudo-absence reflecting search effort" in the Methods section and Figure 5.

-        Formerly Supplementary File 8 - Transferred into the main text, in the subsection "Model evaluation" in the Methods section and Figure 6.

-        Formerly Supplementary File 9 - Renamed as Supplementary File 4.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Using a cross-modal sensory selection task in head-fixed mice, the authors attempted to characterize how different rules reconfigured representations of sensory stimuli and behavioral reports in sensory (S1, S2) and premotor cortical areas (medial motor cortex or MM, and ALM). They used silicon probe recordings during behavior, a combination of single-cell and population-level analyses of neural data, and optogenetic inhibition during the task.

Strengths:

A major strength of the manuscript was the clarity of the writing and motivation for experiments and analyses. The behavioral paradigm is somewhat simple but well-designed and wellcontrolled. The neural analyses were sophisticated, clearly presented, and generally supported the authors' interpretations. The statistics are clearly reported and easy to interpret. In general, my view is that the authors achieved their aims. They found that different rules affected preparatory activity in premotor areas, but not sensory areas, consistent with dynamical systems perspectives in the field that hold that initial conditions are important for determining trial-based dynamics.

Weaknesses:

The manuscript was generally strong. The main weakness in my view was in interpreting the optogenetic results. While the simplicity of the task was helpful for analyzing the neural data, I think it limited the informativeness of the perturbation experiments. The behavioral read-out was low dimensional -a change in hit rate or false alarm rate- but it was unclear what perceptual or cognitive process was disrupted that led to changes in these read-outs. This is a challenge for the field, and not just this paper, but was the main weakness in my view. I have some minor technical comments in the recommendations for authors that might address other minor weaknesses.

I think this is a well-performed, well-written, and interesting study that shows differences in rule representations in sensory and premotor areas and finds that rules reconfigure preparatory activity in the motor cortex to support flexible behavior.

Reviewer #2 (Public Review):

Summary:

Chang et al. investigate neuronal activity firing patterns across various cortical regions in an interesting context-dependent tactile vs visual detection task, developed previously by the authors (Chevee et al., 2021; doi: 10.1016/j.neuron.2021.11.013). The authors report the important involvement of a medial frontal cortical region (MM, probably a similar location to wM2 as described in Esmaeili et al., 2021 & 2022; doi: 10.1016/j.neuron.2021.05.005; doi: 10.1371/journal.pbio.3001667) in mice for determining task rules.

Strengths:

The experiments appear to have been well carried out and the data well analysed. The manuscript clearly describes the motivation for the analyses and reaches clear and well-justified conclusions. I find the manuscript interesting and exciting!

Weaknesses:

I did not find any major weaknesses.

Reviewer #3 (Public Review):

This study examines context-dependent stimulus selection by recording neural activity from several sensory and motor cortical areas along a sensorimotor pathway, including S1, S2, MM, and ALM. Mice are trained to either withhold licking or perform directional licking in response to visual or tactile stimulus. Depending on the task rule, the mice have to respond to one stimulus modality while ignoring the other. Neural activity to the same tactile stimulus is modulated by task in all the areas recorded, with significant activity changes in a subset of neurons and population activity occupying distinct activity subspaces. Recordings further reveal a contextual signal in the pre-stimulus baseline activity that differentiates task context. This signal is correlated with subsequent task modulation of stimulus activity. Comparison across brain areas shows that this contextual signal is stronger in frontal cortical regions than in sensory regions. Analyses link this signal to behavior by showing that it tracks the behavioral performance switch during task rule transitions. Silencing activity in frontal cortical regions during the baseline period impairs behavioral performance.

Overall, this is a superb study with solid results and thorough controls. The results are relevant for context-specific neural computation and provide a neural substrate that will surely inspire follow-up mechanistic investigations. We only have a couple of suggestions to help the authors further improve the paper.

(1) We have a comment regarding the calculation of the choice CD in Fig S3. The text on page 7 concludes that "Choice coding dimensions change with task rule". However, the motor choice response is different across blocks, i.e. lick right vs. no lick for one task and lick left vs. no lick for the other task. Therefore, the differences in the choice CD may be simply due to the motor response being different across the tasks and not due to the task rule per se. The authors may consider adding this caveat in their interpretation. This should not affect their main conclusion.

We thank the Reviewer for the suggestion. We have discussed this caveat and performed a new analysis to calculate the choice coding dimensions using right-lick and left-lick trials (Fig. S3h) on page 8. 

“Choice coding dimensions were obtained from left-lick and no-lick trials in respond-to-touch blocks and right-lick and no-lick trials in respond-to-light blocks. Because the required lick directions differed between the block types, the difference in choice CDs across task rules (Fig. S4f) could have been affected by the different motor responses. To rule out this possibility, we did a new version of this analysis using right-lick and left-lick trials to calculate the choice coding dimensions for both task rules. We found that the orientation of the choice coding dimension in a respond-to-touch block was still not aligned well with that in a respond-to-light block (Fig. S4h;  magnitude of dot product between the respond-to-touch choice CD and the respond-to-light choice CD, mean ± 95% CI for true vs shuffled data: S1: 0.39 ± [0.23, 0.55] vs 0.2 ± [0.1, 0.31], 10 sessions; S2: 0.32 ± [0.18, 0.46] vs 0.2 ± [0.11, 0.3], 8 sessions; MM: 0.35 ± [0.21, 0.48] vs 0.18 ± [0.11, 0.26], 9 sessions; ALM: 0.28 ± [0.17, 0.39] vs 0.21 ± [0.12, 0.31], 13 sessions).”

We also have included the caveats for using right-lick and left-lick trials to calculate choice coding dimensions on page 13.

“However, we also calculated choice coding dimensions using only right- and left-lick trials. In S1, S2, MM and ALM, the choice CDs calculated this way were also not aligned well across task rules (Fig. S4h), consistent with the results calculated from lick and no-lick trials (Fig. S4f). Data were limited for this analysis, however, because mice rarely licked to the unrewarded water port (# of licksunrewarded port  / # of lickstotal , respond-to-touch: 0.13, respond-to-light: 0.11). These trials usually came from rule transitions (Fig. 5a) and, in some cases, were potentially caused by exploratory behaviors. These factors could affect choice CDs.”

(2) We have a couple of questions about the effect size on single neurons vs. population dynamics. From Fig 1, about 20% of neurons in frontal cortical regions show task rule modulation in their stimulus activity. This seems like a small effect in terms of population dynamics. There is somewhat of a disconnect from Figs 4 and S3 (for stimulus CD), which show remarkably low subspace overlap in population activity across tasks. Can the authors help bridge this disconnect? Is this because the neurons showing a difference in Fig 1 are disproportionally stimulus selective neurons?

We thank the Reviewer for the insightful comment and agree that it is important to link the single-unit and population results. We have addressed these questions by (1) improving our analysis of task modulation of single neurons  (tHit-tCR selectivity) and (2) examining the relationship between tHit-tCR selective neurons and tHit-tCR subspace overlaps.  

Previously, we averaged the AUC values of time bins within the stimulus window (0-150 ms, 10 ms bins). If the 95% CI on this averaged AUC value did not include 0.5, this unit was considered to show significant selectivity. This approach was highly conservative and may underestimate the percentage of units showing significant selectivity, particularly any units showing transient selectivity. In the revised manuscript, we now define a unit as showing significant tHit-tCR selectivity when three consecutive time bins (>30 ms, 10ms bins) of AUC values were significant. Using this new criterion, the percentage of tHittCR selective neurons increased compared with the previous analysis. We have updated Figure 1h and the results on page 4:

“We found that 18-33% of neurons in these cortical areas had area under the receiver-operating curve (AUC) values significantly different from 0.5, and therefore discriminated between tHit and tCR trials (Fig. 1h; S1: 28.8%, 177 neurons; S2: 17.9%, 162 neurons; MM: 32.9%, 140 neurons; ALM: 23.4%, 256 neurons; criterion to be considered significant: Bonferroni corrected 95% CI on AUC did not include 0.5 for at least 3 consecutive 10-ms time bins).”

Next, we have checked how tHit-tCR selective neurons were distributed across sessions. We found that the percentage of tHit-tCR selective neurons in each session varied (S1: 9-46%, S2: 0-36%, MM:25-55%, ALM:0-50%). We examined the relationship between the numbers of tHit-tCR selective neurons and tHit-tCR subspace overlaps. Sessions with more neurons showing task rule modulation tended to show lower subspace overlap, but this correlation was modest and only marginally significant (r= -0.32, p= 0.08, Pearson correlation, n= 31 sessions). While we report the percentage of neurons showing significant selectivity as a simple way to summarize single-neuron effects, this does neglect the magnitude of task rule modulation of individual neurons, which may also be relevant. 

In summary, the apparent disconnect between the effect sizes of task modulation of single neurons and of population dynamics could be explained by (1) the percentages of tHit-tCR selective neurons were underestimated in our old analysis, (2) tHit-tCR selective neurons were not uniformly distributed among sessions, and (3) the percentages of tHit-tCR selective neurons were weakly correlated with tHit-tCR subspace overlaps. 

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

For the analysis of choice coding dimensions, it seems that the authors are somewhat data limited in that they cannot compare lick-right/lick-left within a block. So instead, they compare lick/no lick trials. But given that the mice are unable to initiate trials, the interpretation of the no lick trials is a bit complicated. It is not clear that the no lick trials reflect a perceptual judgment about the stimulus (i.e., a choice), or that the mice are just zoning out and not paying attention. If it's the latter case, what the authors are calling choice coding is more of an attentional or task engagement signal, which may still be interesting, but has a somewhat different interpretation than a choice coding dimension. It might be worth clarifying this point somewhere, or if I'm totally off-base, then being more clear about why lick/no lick is more consistent with choice than task engagement.

We thank the Reviewer for raising this point. We have added a new paragraph on page 13 to clarify why we used lick/no-lick trials to calculate choice coding dimensions, and we now discuss the caveat regarding task engagement.  

“No-lick trials included misses, which could be caused by mice not being engaged in the task. While the majority of no-lick trials were correct rejections (respond-to-touch: 75%; respond-to-light: 76%), we treated no-licks as one of the available choices in our task and included them to calculate choice coding dimensions (Fig. S4c,d,f). To ensure stable and balanced task engagement across task rules, we removed the last 20 trials of each session and used stimulus parameters that achieved similar behavioral performance for both task rules (Fig. 1d; ~75% correct for both rules).”

In addition, to address a point made by Reviewer 3 as well as this point, we performed a new analysis to calculate choice coding dimensions using right-lick vs left-lick trials. We report this new analysis on page 8:

“Choice coding dimensions were obtained from left-lick and no-lick trials in respond-to-touch blocks and right-lick and no-lick trials in respond-to-light blocks. Because the required lick directions differed between the block types, the difference in choice CDs across task rules (Fig. S4f) could have been affected by the different motor responses. To rule out this possibility, we did a new version of this analysis using right-lick and left-lick trials to calculate the choice coding dimensions for both task rules. We found that the orientation of the choice coding dimension in a respond-to-touch block was still not aligned well with that in a respond-to-light block (Fig. S4h;  magnitude of dot product between the respond-to-touch choice CD and the respond-to-light choice CD, mean ± 95% CI for true vs shuffled data: S1: 0.39 ± [0.23, 0.55] vs 0.2 ± [0.1, 0.31], 10 sessions; S2: 0.32 ± [0.18, 0.46] vs 0.2 ± [0.11, 0.3], 8 sessions; MM: 0.35 ± [0.21, 0.48] vs 0.18 ± [0.11, 0.26], 9 sessions; ALM: 0.28 ± [0.17, 0.39] vs 0.21 ± [0.12, 0.31], 13 sessions).” 

We added discussion of the limitations of this new analysis on page 13:

“However, we also calculated choice coding dimensions using only right- and left-lick trials. In S1, S2, MM and ALM, the choice CDs calculated this way were also not aligned well across task rules (Fig. S4h), consistent with the results calculated from lick and no-lick trials (Fig. S4f). Data were limited for this analysis, however, because mice rarely licked to the unrewarded water port (# of licksunrewarded port  / # of lickstotal , respond-to-touch: 0.13, respond-to-light: 0.11). These trials usually came from rule transitions (Fig. 5a) and, in some cases, were potentially caused by exploratory behaviors. These factors could affect choice CDs.”

The authors find that the stimulus coding direction in most areas (S1, S2, and MM) was significantly aligned between the block types. How do the authors interpret that finding? That there is no major change in stimulus coding dimension, despite the change in subspace? I think I'm missing the big picture interpretation of this result.

That there is no significant change in stimulus coding dimensions but a change in subspace suggests that the subspace change largely reflects a change in the choice coding dimensions.

As I mentioned in the public review, I thought there was a weakness with interpretation of the optogenetic experiments, which the authors generally interpret as reflecting rule sensitivity. However, given that they are inhibiting premotor areas including ALM, one might imagine that there might also be an effect on lick production or kinematics. To rule this out, the authors compare the change in lick rate relative to licks during the ITI. What is the ITI lick rate? I assume pretty low, once the animal is welltrained, in which case there may be a floor effect that could obscure meaningful effects on lick production. In addition, based on the reported CI on delta p(lick), it looks like MM and AM did suppress lick rate. I think in the future, a task with richer behavioral read-outs (or including other measurements of behavior like video), or perhaps something like a psychological process model with parameters that reflect different perceptual or cognitive processes could help resolve the effects of perturbations more precisely.

Eighteen and ten percent of trials had at least one lick in the ITI in respond-to-touch and  respond-tolight blocks, respectively. These relatively low rates of ITI licking could indeed make an effect of optogenetics on lick production harder to observe. We agree that future work would benefit from more complex tasks and measurements, and have added the following to make this point (page 14):

“To more precisely dissect the effects of perturbations on different cognitive processes in rule-dependent sensory detection, more complex behavioral tasks and richer behavioral measurements are needed in the future.”

Reviewer #2 (Recommendations For The Authors):

I have the following minor suggestions that the authors might consider in revising this already excellent manuscript :

(1) In addition to showing normalised z-score firing rates (e.g. Fig 1g), I think it is important to show the grand-average mean firing rates in Hz.

We thank the Reviewer for the suggestion and have added the grand-average mean firing rates as a new supplementary figure (Fig. S2a). To provide more details about the firing rates of individual neurons, we have also added to this new figure the distribution of peak responses during the tactile stimulus period (Fig. S2b).

(2) I think the authors could report more quantitative data in the main text. As a very basic example, I could not easily find how many neurons, sessions, and mice were used in various analyses.

We have added relevant numbers at various points throughout the Results, including within the following examples:

Page 3: “To examine how the task rules influenced the sensorimotor transformation occurring in the tactile processing stream, we performed single-unit recordings from sensory and motor cortical areas including S1, S2, MM and ALM (Fig. 1e-g, Fig. S1a-h, and Fig. S2a; S1: 6 mice, 10 sessions, 177 neurons, S2: 5 mice, 8 sessions, 162 neurons, MM: 7 mice, 9 sessions, 140 neurons, ALM: 8 mice, 13 sessions, 256 neurons).”

Page 5: “As expected, single-unit activity before stimulus onset did not discriminate between tactile and visual trials (Fig. 2d; S1: 0%, 177 neurons; S2: 0%, 162 neurons; MM: 0%, 140 neurons; ALM: 0.8%, 256 neurons). After stimulus onset, more than 35% of neurons in the sensory cortical areas and approximately 15% of neurons in the motor cortical areas showed significant stimulus discriminability (Fig. 2e; S1: 37.3%, 177 neurons; S2: 35.2%, 162 neurons; MM: 15%, 140 neurons; ALM: 14.1%, 256 neurons).”

Page 6: “Support vector machine (SVM) and Random Forest classifiers showed similar decoding abilities

(Fig. S3a,b; medians of classification accuracy [true vs shuffled]; SVM: S1 [0.6 vs 0.53], 10 sessions, S2

[0.61 vs 0.51], 8 sessions, MM [0.71 vs 0.51], 9 sessions, ALM [0.65 vs 0.52], 13 sessions; Random

Forests: S1 [0.59 vs 0.52], 10 sessions, S2 [0.6 vs 0.52], 8 sessions, MM [0.65 vs 0.49], 9 sessions, ALM [0.7 vs 0.5], 13 sessions).”

Page 6: “To assess this for the four cortical areas, we quantified how the tHit and tCR trajectories diverged from each other by calculating the Euclidean distance between matching time points for all possible pairs of tHit and tCR trajectories for a given session and then averaging these for the session (Fig. 4a,b; S1: 10 sessions, S2: 8 sessions, MM: 9 sessions, ALM: 13 sessions, individual sessions in gray and averages across sessions in black; window of analysis: -100 to 150 ms relative to stimulus onset; 10 ms bins; using the top 3 PCs; Methods).” 

Page 8: “In contrast, we found that S1, S2 and MM had stimulus CDs that were significantly aligned between the two block types (Fig. S4e; magnitude of dot product between the respond-to-touch stimulus CDs and the respond-to-light stimulus CDs, mean ± 95% CI for true vs shuffled data: S1: 0.5 ± [0.34, 0.66] vs 0.21 ± [0.12, 0.34], 10 sessions; S2: 0.62 ± [0.43, 0.78] vs 0.22 ± [0.13, 0.31], 8 sessions; MM: 0.48 ± [0.38, 0.59] vs 0.24 ± [0.16, 0.33], 9 sessions; ALM: 0.33 ± [0.2, 0.47] vs 0.21 ± [0.13, 0.31], 13 sessions).”  Page 9: “For respond-to-touch to respond-to-light block transitions, the fractions of trials classified as respond-to-touch for MM and ALM decreased progressively over the course of the transition (Fig. 5d; rank correlation of the fractions calculated for each of the separate periods spanning the transition, Kendall’s tau, mean ± 95% CI: MM: -0.39 ± [-0.67, -0.11], 9 sessions, ALM: -0.29 ± [-0.54, -0.04], 13 sessions; criterion to be considered significant: 95% CI on Kendall’s tau did not include 0).

Page 11: “Lick probability was unaffected during S1, S2, MM and ALM experiments for both tasks, indicating that the behavioral effects were not due to an inability to lick (Fig. 6i, j; 95% CI on Δ lick probability for cross-modal selection task: S1/S2 [-0.18, 0.24], 4 mice, 10 sessions; MM [-0.31, 0.03], 4 mice, 11 sessions; ALM [-0.24, 0.16], 4 mice, 10 sessions; Δ lick probability for simple tactile detection task: S1/S2 [-0.13, 0.31], 3 mice, 3 sessions; MM [-0.06, 0.45], 3 mice, 5 sessions; ALM [-0.18, 0.34], 3 mice, 4 sessions).”

(3) Please include a clearer description of trial timing. Perhaps a schematic timeline of when stimuli are delivered and when licking would be rewarded. I may have missed it, but I did not find explicit mention of the timing of the reward window or if there was any delay period.

We have added the following (page 3): 

“For each trial, the stimulus duration was 0.15 s and an answer period extended from 0.1 to 2 s from stimulus onset.”

(4) Please include a clear description of statistical tests in each figure legend as needed (for example please check Fig 4e legend).

We have added details about statistical tests in the figure legends:

Fig. 2f: “Relationship between block-type discriminability before stimulus onset and tHit-tCR discriminability after stimulus onset for units showing significant block-type discriminability prior to the stimulus. Pearson correlation: S1: r = 0.69, p = 0.056, 8 neurons; S2: r = 0.91, p = 0.093, 4 neurons; MM: r = 0.93, p < 0.001, 30 neurons; ALM: r = 0.83, p < 0.001, 26 neurons.” 

Fig. 4e: “Subspace overlap for control tHit (gray) and tCR (purple) trials in the somatosensory and motor cortical areas. Each circle is a subspace overlap of a session. Paired t-test, tCR – control tHit: S1: -0.23, 8 sessions, p = 0.0016; S2: -0.23, 7 sessions, p = 0.0086; MM: -0.36, 5 sessions, p = <0.001; ALM: -0.35, 11 sessions, p < 0.001; significance: ** for p<0.01, *** for p<0.001.”  

Fig. 5d,e: “Fraction of trials classified as coming from a respond-to-touch block based on the pre-stimulus population state, for trials occurring in different periods (see c) relative to respond-to-touch → respondto-light transitions. For MM (top row) and ALM (bottom row), progressively fewer trials were classified as coming from the respond-to-touch block as analysis windows shifted later relative to the rule transition. Kendall’s tau (rank correlation): MM: -0.39, 9 sessions; ALM: -0.29, 13 sessions. Left panels: individual sessions, right panels: mean ± 95% CI. Dash lines are chance levels (0.5). e, Same as d but for respond-to-light → respond-to-touch transitions. Kendall’s tau: MM: 0.37, 9 sessions; ALM: 0.27, 13 sessions.”

Fig. 6: “Error bars show bootstrap 95% CI. Criterion to be considered significant: 95% CI did not include 0.”

(5) P. 3 - "To examine how the task rules influenced the sensorimotor transformation occurring in the tactile processing stream, we performed single-unit recordings from sensory and motor cortical areas including S1, S2, MM, and ALM using 64-channel silicon probes (Fig. 1e-g and Fig. S1a-h)." Please specify if these areas were recorded simultaneously or not.

We have added “We recorded from one of these cortical areas per session, using 64-channel silicon probes.”  on page 3.  

(6) Figure 4b - Please describe what gray and black lines show.

The gray traces are the distance between tHit and tCR trajectories in individual sessions and the black traces are the averages across sessions in different cortical areas. We have added this information on page 6 and in the Figure 4b legend. 

Page 6: “To assess this for the four cortical areas, we quantified how the tHit and tCR trajectories diverged from each other by calculating the Euclidean distance between matching time points for all possible pairs of tHit and tCR trajectories for a given session and then averaging these for the session (Fig. 4a,b; S1: 10 sessions, S2: 8 sessions, MM: 9 sessions, ALM: 13 sessions, individual sessions in gray and averages across sessions in black; window of analysis: -100 to 150 ms relative to stimulus onset; 10 ms bins; using the top 3 PCs; Methods).

Fig. 4b: “Distance between tHit and tCR trajectories in S1, S2, MM and ALM. Gray traces show the time varying tHit-tCR distance in individual sessions and black traces are session-averaged tHit-tCR distance (S1:10 sessions; S2: 8 sessions; MM: 9 sessions; ALM: 13 sessions).”

(7) In addition to the analyses shown in Figure 5a, when investigating the timing of the rule switch, I think the authors should plot the left and right lick probabilities aligned to the timing of the rule switch time on a trial-by-trial basis averaged across mice.

We thank the Reviewer for suggesting this addition. We have added a new figure panel to show the probabilities of right- and left-licks during rule transitions (Fig. 5a).

Page 8: “The probabilities of right-licks and left-licks showed that the mice switched their motor responses during block transitions depending on task rules (Fig. 5a, mean ± 95% CI across 12 mice).” 

(8) P. 12 - "Moreover, in a separate study using the same task (Finkel et al., unpublished), high-speed video analysis demonstrated no significant differences in whisker motion between respond-to-touch and respond-to-light blocks in most (12 of 14) behavioral sessions.". Such behavioral data is important and ideally would be included in the current analysis. Was high-speed videography carried out during electrophysiology in the current study?

Finkel et al. has been accepted in principle for publication and will be available online shortly. Unfortunately we have not yet carried out simultaneous high-speed whisker video and electrophysiology in our cross-modal sensory selection task.

Reviewer #3 (Recommendations For The Authors):

(1) Minor point. For subspace overlap calculation of pre-stimulus activity in Fig 4e (light purple datapoints), please clarify whether the PCs for that condition were constructed in matched time windows. If the PCs are calculated from the stimulus period 0-150ms, the poor alignment could be due to mismatched time windows.

We thank the Reviewer for the comment and clarify our analysis here. We previously used timematched windows to calculate subspace overlaps. However, the pre-stimulus activity was much weaker than the activity during the stimulus period, so the subspaces of reference tHit were subject to noise and we were not able to obtain reliable PCs. This caused the subspace overlap values between the reference tHit and control tHit to be low and variable (mean ± SD, S1:  0.46± 0.26, n = 8 sessions, S2: 0.46± 0.18, n = 7 sessions, MM: 0.44± 0.16, n = 5 sessions, ALM: 0.38± 0.22, n = 11 sessions).  Therefore, we used the tHit activity during the stimulus window to obtain PCs and projected pre-stimulus and stimulus activity in tCR trials onto these PCs. We have now added a more detailed description of this analysis in the Methods (page 32). 

“To calculate the separation of subspaces prior to stimulus delivery, pre-stimulus activity in tCR trials (100 to 0 ms from stimulus onset) was projected to the PC space of the tHit reference group and the subspace overlap was calculated. In this analysis, we used tHit activity during stimulus delivery (0 to 150 ms from stimulus onset) to obtain reliable PCs.”   

We acknowledge this time alignment issue and have now removed the reported subspace overlap between tHit and tCR during the pre-stimulus period from Figure 4e (light purple). However, we think the correlation between pre- and post- stimulus-onset subspace overlaps should remain similar regardless of the time windows that we used for calculating the PCs. For the PCs calculated from the pre-stimulus period (-100 to 0 ms), the correlation coefficient was 0.55 (Pearson correlation, p <0.01, n = 31 sessions). For the PCs calculated from the stimulus period (0-150 ms), the correlation coefficient was 0.68 (Figure 4f, Pearson correlation, p <0.001, n = 31 sessions). Therefore, we keep Figure 4f.  

(2) Minor point. To help the readers follow the logic of the experiments, please explain why PPC and AMM were added in the later optogenetic experiment since these are not part of the electrophysiology experiment.

We have added the following rationale on page 9.

“We recorded from AMM in our cross-modal sensory selection task and observed visually-evoked activity (Fig. S1i-k), suggesting that AMM may play an important role in rule-dependent visual processing. PPC contributes to multisensory processing51–53 and sensory-motor integration50,54–58.  Therefore, we wanted to test the roles of these areas in our cross-modal sensory selection task.”

(3) Minor point. We are somewhat confused about the timing of some of the example neurons shown in figure S1. For example, many neurons show visually evoked signals only after stimulus offset, unlike tactile evoked signals (e.g. Fig S1b and f). In addition, the reaction time for visual stimulus is systematically slower than tactile stimuli for many example neurons (e.g. Fig S1b) but somehow not other neurons (e.g. Fig S1g). Are these observations correct?

These observations are all correct. We have a manuscript from a separate study using this same behavioral task (Finkel et al., accepted in principle) that examines and compares (1) the onsets of tactile- and visually-evoked activity and (2) the reaction times to tactile and visual stimuli. The reaction times to tactile stimuli were slightly but significantly shorter than the reaction times to visual stimuli (tactile vs visual, 397 ± 145 vs 521 ± 163 ms, median ± interquartile range [IQR], Tukey HSD test, p = 0.001, n =155 sessions). We examined how well activity of individual neurons in S1 could be used to discriminate the presence of the stimulus or the response of the mouse. For discriminability for the presence of the stimulus, S1 neurons could signal the presence of the tactile stimulus but not the visual stimulus. For discriminability for the response of the mouse, the onsets for significant discriminability occurred earlier for tactile compared with visual trials (two-sided Kolmogorov-Smirnov test, p = 1x10-16, n = 865 neurons with DP onset in tactile trials, n = 719 neurons with DP onset in visual trials).

Author response:

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

eLife assessment

This is a valuable study that describes the effects of T. pallidum on neural development by applying single-cell RNA sequencing to an iPSC-derived brain organoid model. The evidence supporting the claims of the authors is solid, although further evidence to understand the differences in infection rates would strengthen the conclusions of the study. In particular, the conclusions would be strengthened by validating infection efficiency as this can impact the interpretation of single-cell sequencing results, and how these metrics affect organoid size as well as comparison with additional infectious agents. Furthermore, additional validations of downstream effectors are not adequate and could be improved. 

Thank you very much for your valuable comments. Since we used the organoid model for the first time to investigate the effects of T. pallidum on brain development, the study design is not perfect. As you have accurately mentioned, the results of the paper do not have more in-depth details, especially to verify the infection rate of T. pallidum. Your valuable comments will be very useful for us for carrying out further research. In addition, the downstream effector validation is inadequate, so we performed an analysis of single-cell sequencing data to strengthen our view in the revised manuscript (See Figure 5F for a description in current manuscript).

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This is an interesting study by Xu et al showing the effects of infection with the Treponema pallidum virus (which causes syphilis disease) on neuronal development using iPSC-derived human brain organoids as a model and single-cell RNA sequencing. This work provides an important insight into the impact of the virus on human development, bridging the gap between the phenomena observed in studies using animal models as well as non-invasive human studies showing developmental abnormalities in fetuses infected with the virus in utero through maternal vertical transmission.

Using single-cell RNAseq in combination with qPCR and immunofluorescence techniques, the authors show that T. pallidum infected organoids are smaller in size, in particular during later growth stages, contain a larger number of undifferentiated neuronal lineage cells, and exhibit decreased numbers of specific neuronal subcluster, which the authors have identified as undifferentiated hindbrain neurons.

The study is an important first step in understanding how T. pallidum affects human neuronal development and provides important insight into the potential mechanisms that underlie the neurodevelopmental abnormalities observed in infected human fetuses. Several important weaknesses have also been noted, which need to be addressed to strengthen the study's conclusions.

Strengths:

(1) The study is well written, and the data quality is good for the most part.

(2) The study provides an important first step in utilizing human brain organoids to study the impact of T. pallidum infection on neuronal development.

(3) The study's conclusions may provide important insight to other researchers focused on studying how viral infections impact neuronal development. 

Thank you very much for your positive feedback. Below, you will find our detailed responses to your concerns, addressed point-by-point. I once again sincerely appreciate your time and effort in reviewing our manuscript.

Weaknesses:

(1) It is unclear how T. pallidum infection was validated in the organoids. If not all cells are infected, this could have important implications for the study's conclusions, in particular the single-cell RNAseq experiments. Were only cells showing the presence of the virus selected for sequencing? A detailed description of how infection was validated and the process of selection of cells for RNAseq would strongly support the study's conclusions. 

Thank you for your valuable comment. We completely agree with your point. Exploring the infection rate of T. pallidum to brain organoids is a key factor that must be considered. We selected pluripotent stem cell-derived brain organoids to simulate the process of foetal brain neurodevelopment and cultured them mixed with T. pallidum to mimic T. pallidum invading brain tissue. Since brain organoids are three-dimensional structures formed by nerve cell aggregation, T. pallidum invades organoids from the periphery to the center of the organoids gradually. T. pallidum acts on organoids long enough to increase the infection rates; however, the pathogen is selective in invading human cells. If we only select cells present in T. pallidum for sequencing, the authenticity of simulating "real world" infections is somewhat weakened. To better carry out this study, selecting cells from intact organoids for sequencing, without eliminating cells without T. pallidum, can better simulate the effect of T. pallidum infection on the nervous system. Of course, we should also set up a blank control group.

(2) The authors show that T. pallidum infection results in impaired development of hindbrain neurons. How does this finding compare to what has already been shown in animal studies? Is a similar deficit in this brain region observed with this specific virus? It would be useful to strengthen the study's conclusions if the authors added a discussion about the observed deficits in hindbrain neuronal development, and prior literature on similar studies conducted in animal models or human patients. Does T. pallidum preferentially target these neurons, or is this a limitation of the current organoid model system? 

Thank you for your valuable comments. The finding that T. pallidum infection results in impaired development of hindbrain neurons has not been verified in animal experiments. Of course, it is better to further validate the findings in organoid studies through animal experiments. Unfortunately, due to the technical challenges, mature animal models have not been developed for the study of congenital syphilis. Although our team has been working on the development of animal models of congenital neurosyphilis, the current progress is still not satisfactory. After struggling hard in this field for many years, we decided to attempt to utilize human brain organoids instead of animal models to study the impact of T. pallidum infection on neuronal development.

We also checked prior literature on similar studies that have referred to the content in human patients. Dan Doherty et al. reported that patients with pontocerebellar hypoplasia develop microcephaly at birth or over time after birth (PMID: 23518331). Based on your constructive suggestions, we have added some content related to hindbrain to the “Discussion” section.

Our study found that T. pallidum could inhibit the differentiation of subNPC1B in brain organoids, thereby reducing the differentiation from subNPC1B to hindbrain neurons, and ultimately affecting the development and maturation of hindbrain neurons during pregnancy. Based on our results, T. pallidum does not preferentially target hindbrain neurons. Of course, there are limitations to the current organoid model system, see the "Limitations" section.

PMID: 23518331- Dan Doherty et al, Midbrain and hindbrain malformations: advances in clinical diagnosis, imaging, and genetics.

Revision in the “Discussion” section, line 343-352:

“The vertebrate hindbrain contains a complex network of dedicated neural circuits that play an essential role in controlling many physiological processes and behaviors, including those related to the cerebellum, pons, and medulla oblongata (Shoja et al., 2018). Patients with pontocerebellar hypoplasia represent the less severe end of the spectrum with early hyperreflexia, developmental delay, and feeding problems, eventually developing spasticity and involuntary movements in childhood, while some patients represent the severe end of the spectrum characterised by polyhydramnios, severe hyperreflexia, contracture, and early death from central respiratory failure. Patients with pontocerebellar hypoplasia develop microcephaly at birth or over time after birth (Doherty et al., 2013).”

(3) The authors show that T. pallidum-infected organoids are smaller in size by measuring organoid diameter during later stages of organoid growth, with no change during early stages. Does that represent insufficient infection at the early stages? Is this due to increased cell death or lack of cell division in the infected organoids? Experiments using IHC to quantify levels of cleaved caspase and/or protein markers for cell proliferation would be able to address these questions. 

Thank you for your valuable suggestion. The concentration of T. pallidum in patients with syphilis was generally very low (PMID: 21752804, 35315702, 33099614). In this study, a low concentration of T. pallidum was applied to brain organoids to simulate early foetal transmission of syphilis. Nerve cells mainly establish intercellular connections to form brain organoids in the way of adhesion, which can easily cause organoids to divide and die if treated with a high concentration of T. pallidum. Furthermore, based on your suggestions, we performed additional immunostaining analyses to verify the apoptosis of brain organoids infected by T. pallidum. Cleaved caspase 3 (clCASP3) staining showed that the number of apoptotic cells increased following T. pallidum infection; however, the proportion of apoptotic cells in both groups of brain organoids was very low (Figure supplement 2) (N=12 organoids, each group from three independent bioreactors), which would be not enough to affect the results of the experiment, thereby suggesting that neural differentiation and development of brain organoids were mainly inhibited following T. pallidum infection (rather than promoting organoid apoptosis).

PMID: 21752804-- Craig Tipple et al, Getting the measure of syphilis: qPCR to better understand early infection.

PMID: 35315702-- Cuini Wang et al, Quantified Detection of Treponema pallidum DNA by PCR Assays in Urine and Plasma of Syphilis Patients.

PMID: 33099614—Cuini Wang et al, A New Specimen for Syphilis Diagnosis: Evidence by High Loads of Treponema pallidum DNA in Saliva.

Revision in the “Results” section, line 105-108:

“… cleaved caspase 3 (clCASP3) staining showed that the number of apoptotic cells increased significantly following T. pallidum infection, but the proportion of apoptotic cells in both groups of brain organoids was very low (Figure supplement 2) (N=12 organoids, each group from three independent bioreactors) …”

Revision in the “Materials and methods” section, line 446-447:

“…anti-cleaved caspase 3 (rabbit, 1:100, Cell Signaling Technology, 9661S),”

Revision in the “Supplementary File” section, line 78-81:

Author response image 1.

The number of clCASP3+ cells in the microscopic field of brain organoids. A nonparametric t-test was used to evaluate the statistical differences between the two groups. (**: P < 0.01).

(4) In Figure 1D authors show differences in rosette-like structure in the infected organoids. The representative images do not appear to be different in any of the discussed components (e.g., the sox2 signal looks fairly similar between the two conditions). No quantification of these structures was presented. Authors should provide quantification or a more representative image to support their statement. 

Thank you for your valuable suggestion. I have quantified the neural rosette structure and compared the number of intact rosette-like structures between the two groups (See Figure 1D for a description in current manuscript).

(5) The IHC images shown in Figures 3E, G, and Figure 4E look very similar between the two conditions despite the discussed decrease in the text. A more suitable representative image should be presented, or the analysis should be amended to reflect the observed results. 

Thank you for your valuable suggestion. I have replaced more representative images in Figure 3E, G, and Figure 4E in the manuscript.

Reviewer #2 (Public Review):

Summary:

This study provides an important overview of infectious etiology for neurodevelopment delay.

Strengths:

Strong RNA evaluation.

Weaknesses:

The study lacks an overview of other infectious agents. The study should address the epigenetic contributors (PMID: 36507115) and the role of supplements in improving outcomes (PMID: 27705610). 

Addressing the above - with references included - is recommended. 

Thank you for your valuable comment. Our research is mainly inspired by other infectious agents, such as Zika virus; there are many descriptions of Zika virus in the “Discussion” section of the manuscript to better describe and demonstrate our point of view (See pages 12–13). I was unable to retrieve the article (PMID: 36507115), kindly help in confirming the PMID number. I will be very grateful if you can provide the full text. Secondly, I have carefully read the article (PMID: 27705610), which is a very rich and comprehensive review, and summarised and cited it in appropriate places in our manuscript.

Revision in the “Discussion- limitation” section, line 375-379:

“First, although several recent protocols have made use of growth factors to promote further neuronal maturation and survival (Lucke-Wold et al., 2018), the organoid culture scheme needs to be further improved owing to the lower percentage of mature neurons and the challenge of cell necrosis within the organoids at this stage in day 55 organoids.”

Reviewer #3 (Public Review): 

This article is the first report to study the effects of T. pallidum on the neural development of an iPSC-derived brain organoid model. The study indicates that T. pallidum inhibits the differentiation of subNPC1B neurons into hindbrain neurons, hence affecting brain organoid neurodevelopment. Additionally, the TCF3 and notch signaling pathways may be involved in the inhibition of the subNPC1B-hindbrain neuron differentiation axis. While the majority of the data in this study support the conclusions, there are still some questions that need to be addressed and data quality needs to be improved. The study provides valuable insights for future investigations into the mechanisms underlying congenital neurodevelopment disability. 

I sincerely appreciate your comments on our paper. The comments have helped us greatly improve the quality of our paper. Thank you for your time and constructive critique.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Paired t-test analysis is not appropriate if two distinct groups are compared. 

I sincerely apologize for our presentation. We used a nonparametric t-test to compare the two groups. I have confirmed and corrected the statistical method description of this manuscript (Revision in the “Materials and methods” section (line 553-555) and “Figures-legend” section (line 789-790, 817-818, 829-830) in current manuscript).

Reviewer #3 (Recommendations For The Authors): 

(1) Can the authors explain why the mean size of organoids infected with T. pallidum is smaller?

Thank you for your valuable comment. In our study, T. pallidum infection resulted in brain organisational changes in neural rosette-like structures resembling the proliferative regions of the human ventricular zone and caused fewer and incomplete rosette-like structures. Next, the ventricular zone is also the main area where neural progenitor cells (NPCs) reside (PMID: 33838105); our results showed that the proportion of neural progenitor cells (NPC)1 was reduced after T. pallidum infection. Rosette-like structure size changes owing to NPC depletion. Therefore, the mean size of organoids infected with T. pallidum is smaller.

Revision in the “Results” section, line 101-104:

“T. pallidum infection resulted in brain organisational changes in neural rosette-like structures resembling the proliferative regions of the human ventricular zone where NPC reside (Krenn et al., 2021), and caused fewer and incomplete rosette-like structures (P < 0.01) (Figure 1D)”

(2) Why was the target gene for qRT-PCR validation selected to be HOXA5、HOXC5、HOXA4?

Thank you for your valuable comment. The qRT-PCR experiment was selected here to verify the analysis results of the scRNA-seq. HOX family genes are key factors controlling early hindbrain development, which are expressed in the hindbrain region during the gastrulation stage of early embryonic development and persist into the nerve cell stage, and are essential for the correct induction of hindbrain development and segmentation (PMID: 2571936, 1983472, 1673098, 15930115). Therefore, we selected the HOX family gene for verification.

PMID: 2571936-WILKINSON D G, et al. Segmental expression of Hox-2 homoeobox- containing genes in the developing mouse hindbrain.

PMID: 1983472-- FROHMAN M A, et al. Isolation of the mouse Hox-2.9 gene; analysis of embryonic expression suggests that positional information along the anterior-posterior axis is specified by mesoderm.

PMID: 1673098--MURPHY P, et al. Expression of the mouse labial-like homeobox-containing genes, Hox 2.9 and Hox 1.6, during segmentation of the hindbrain.

PMID: 15930115-- MCNULTY C L, et al. Knockdown of the complete Hox paralogous group 1 leads to dramatic hindbrain and neural crest defects.

(3) Why was qRT-PCR not employed in other experimental validations, but solely to validate early neural-specific transcription factor changes?

Thank you for your valuable comment. The qRT-PCR experiment was selected to validate early neural-specific transcription factor changes, indicating the reliability of the scRNA-seq. Then, validated scRNA-seq data were used to analyze for other neuro-specific gene differences, such as violin plots and heatmap showing differentially expressed genes (Figure 4D and Figure 5B, C). Of course, we also tested it with other experiments, such as immunohistochemistry and flow cytometric screening.

(4) The authors found that T. pallidum might reduce the differentiation from subNPC1B to hindbrain neurons by inhibiting subNPC1B differentiation in brain organoids. Why were the subNPC1B-specific markers declining?

Thank you for your valuable comment. scRNA-seq is aimed at complete brain organoids. Cluster analysis of cell types of organoids is performed according to specific marker genes of different cells. The decrease in the expression of marker genes of certain cell groups indicates that the cell proportion of such cell groups in the whole organoids is reduced. We analysed organoids following T. pallidum infection, uniform manifold approximation and projection (UMAP), and clustering of the NPC1 population demonstrated that T. pallidum downregulated the number of subNPC1B population. Therefore, the results demonstrated a decrease in the subNPC1B -specific markers.

(5) In comparison to the other figures, Figure 5E letter size is excessively small and ambiguous.

Thanks for your valuable comments, I have adjusted Figure 5E letter size.

(6) Figure 5E shows that TCF3, more than one gene, is specifically enriched in subNPC1B of the T. pallidum group. It is best to confirm the impact of the other gene. 

Thank you for raising this key issue that we had not addressed properly in our previous version of the manuscript; we have added further analytical data. The SCENIC analysis found that the transcriptional activity of 52 genes has significantly changed after T. pallidum infection. Furthermore, GO analyses demonstrated that 27 transcription factors were significantly enriched in four key pathways of neural differentiation and development. TCF3 is the sole transcription factor present in all four terms simultaneously, speculating that TCF3 is the key transcription factor for the inhibition of subNPC1B-hindbrain neuron differentiation caused by T. pallidum.

Revision in the “Results” section, line 261-273:

“Next, the single-cell regulatory network inference and clustering (SCENIC) analysis for the subNPC1B subcluster was performed to assess the differences in the transcriptional activity of the transcription factors between the two groups and found that the transcriptional activity of 52 genes significantly changed after T. pallidum infection (Figure 5E). Furthermore, GO analyses demonstrated that 27 transcription factors were significantly enriched in key pathways of neural differentiation and development in response to nervous system development, positive regulation of sequence-specific DNA-binding transcription factor activity, positive regulation of neuronal differentiation, and DNA templated transcription regulation. Remarkably, transcription factor 3 (TCF3) is the sole transcription factor present in all four terms simultaneously (Figure 5F), speculating that TCF3 is the key transcription factor for the inhibition of subNPC1B-hindbrain neuron differentiation caused by T. pallidum.”

Revision in the “Materials and methods” section, line 540-543:

“The Sankey diagram was created using SankeyMATIC (https://sankeymatic.com/) (Zhang et al., 2023), which was used to characterize the interactions between differential transcription factors and neural differentiation and development.”

Revision in the “Figure and Figure Legend” section, line 832, 842-844:

Author response image 2.

Sankey diagram showing the correspondence between differential transcription factors and neural differentiation and development.

(7) Are there other experiments demonstrating that TCF3 is a key transcription factor for the inhibition of subNPC1B-hindbrain neuron differentiation caused by T. pallidum? 

Thank you for your valuable comment. In the previous experiment, we attempted to select a subNPC1B subcluster by flow sorting to verify the relevant molecular mechanism. Due to the small proportion of subNPC1B subcluster in the whole organoids, the selected cells were in a poor state and could not reach the number of cells required for the experiment. However, we used scRNA-seq data to further identify TCF3 as a key transcription factor that inhibits subNPC1B - hindbrain neuron differentiation induced by T. pallidum. The relevant results and descriptions of the analysis are detailed in the revised manuscript, please see our response to point (6) above.

Author response:

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

Reviewer #1 (Public Review):

Summary:

The authors use the innovative CRISPRi method to uncover regulators of cell density and volume in neutrophils. The results show that cells require NHE activity during chemoattractant-driven cell migration. Before migration occurs, cells also undergo a rapid cell volume increase. These results indicate that water flux, driven by ion channels, appears to play a central role in neutrophil migration. The paper is very well written and clear. I suggest adding some discussion about the role of actin in the process, but this is not essential.

Strengths

The novel use of CRIPSPi to uncover cell density regulators is very novel. Some of the uncovered molecules were known before, e.g. discussed in Li & Sun, Frontiers in Cell and Developmental Biology, 2021. Others are more interesting, for example PI3K-gamma. The use of caged fMLP is also nice.

We thank the reviewer for their positive appraisal of our work and have pursued their suggestions for improving our paper in this revision.

Weaknesses

One area of investigation that seems to be absent is mentioned in the introduction. I.e., actin is expected to play a role in regulating cell volume increase. Did the authors perform any experiments with LatA? What was seen there? Do cells still migrate with LatA, or is a different interplay seen? The role of PI3K is interesting, and maybe somewhat related to actin. But this may be a different line of inquiry for the future.

We agree that we could have done a better job explicitly investigating the role of actin dynamics in volume changes. Towards this end, by using Latrunculin B to depolymerize actin, we find that the volume increase in suspension is not affected (Figure 1 – supplemental figure 2A). In our FxM single cell volume measurements of adherent cells, we similarly observed unhindered swelling following latrunculin treatment. These data indicate that actin is dispensable for chemoattractant-induced cell swelling (Figure 1 – supplemental figure 2B) . There was a minor apparent reduction in the final volume reached with the Latrunculin-treated cells as measured by FxM, but this likely reflects minor uptake of the excluded dye following Latrunculin treatment rather than an actual change in final volume. This conclusion is reinforced by the change in 2D footprint area being well modeled by the 2D projection of an isotropically expanding sphere (Figure 1 – supplemental figure 2C) . Latrunculin treatment completely abolishes migration, as is expected for unconfined migration on fibronectin (Figure 1 – supplemental figure 2D-E) . The second Reviewer also wanted us to dig deeper on the role of PI3K-gamma, so we expanded our analysis of this hit (Figure 3 – supplemental figure 1B-D; Figure 4 – supplemental figure 1D-G) .

Author response image 1.

Chemoattractant-induced swelling, but not motility, is independent of actin polymerization. (A) Human primary neutrophils were incubated with DMSO or Latrunculin B, activated with 20 nM fMLP, and then volume responses were measured using electronic sizing via a Coulter counter. Latrunculin treatment did not alter cell swelling, indicating that actin polymerization is dispensable for the chemoattractant-induced volume increase. (B) Similar results were obtained using the FxM assay, showing that Latrunculin-treated cells are capable of swelling after stimulation. (C) The Latrunculin-treated cells also increase their footprints, albeit less so than control cells, but this is within the range of what would be expected for this degree of chemoattractant-induced volume increase (modeled by a sphere expanding an equivalent volume). (D) Single cell tracks of primary human neutrophils responding to acute chemoattractant stimulation. Both panels show 15 minutes of tracks with the tracks prior (left) and the 15 minutes post (right) uncaging the chemoattractant. The scale bar is 50 microns. The top panels show the large increase in motility displayed by control cells, while the Latrunculin-treated cells (bottom panels) fail to move. (E) Latrunculin-treated cells consistently fail to move in response to chemoattractant-stimulation. (F) Representative single cell volume traces show that Latrunculin-treated cells (black) lack short-term volume fluctuations but persistently maintain an elevated volume following chemoattractant stimulation. Control cells (blue) exhibit short-term volume fluctuations. (G) The lack of short-term volume fluctuations following latrunculin treatment is borne out across the population, with the coefficient of variation in the volume for single cells (post-swelling) being dramatically lower in Latrunculin-treated cells, suggesting that these short term volume fluctuations depend on actin-based motility.

Author response image 2.

Additional validation of swelling screen hits. (A) Mixed WT and CRISPR KO dHL-60 populations post-stimulation show that CA2 (black) and PI3Ky (green) KO both fail to decrease their densities as much as the WT (cyan) population following chemoattractant stimulation. Cells with negative control guides (light gray) have normal volume responses. All tubes were fractionated and aligned on the fraction containing the median of the WT population. Negative values indicate a fraction with a higher density than WT. (B) To validate the perturbations to cell swelling observed with FxM, primary human neutrophils were stimulated in suspension, and their volumes were measured using a Coulter counter. 20 nM fMLP was added at the 0 minute mark. Shaded regions represent the 95% confidence intervals. (C) PI3Kγ inhibition blocks the chemoattractant-induced volume change in primary human neutrophils, as assayed by FxM. (D) PI3Kγ inhibition also blocked the chemoattractant-drive shape change in human primary neutrophils, as measured by the change in footprint area in FxM (E) The coefficient of variation in volume for control (cyan) and iNHE1 (gold) inhibited human primary neutrophils undergoing chemokinesis are comparable, suggesting that the volume fluctuations are unchanged in moving cells upon NHE1 and PI3Kγ inhibition despite the different baseline volumes.

Author response image 3.

Additional validation of motility phenotypes. (A-D) Single cell tracks of primary human neutrophils responding to acute chemoattractant stimulation. Both panels show tracks of cells 15 minutes prior (left) versus 15 minutes post (right) uncaging the chemoattractant. The scale bar is 50 microns. Color saturation indicates time with tracks progressing from gray to full color. (A) Control cells show a large increase in movement upon uncaging, (B) NHE1 inhibited cells also initiate movement but to a lesser degree, (C) hypo-osmotic shock rescues the NHE1 motility defect. (D) PI3Kγ leads to a large fraction of cells failing to initiate movement. (E) PI3Kγ inhibition showed near complete blockage of the chemoattractant-induced motility increase in primary human neutrophils. (F) Control neutrophils (blue) show an increased angular alignment upon stimulation as their motility becomes directional. NHE1-inhibition (gold, iNHE1) has very little effect on this process, while PI3Kγ inhibition (green) leads to a reduction in this alignment at the population level. (G) For the PI3Kγ inhibited cells that start migrating, the migration-induced volume fluctuations are comparable to iNHE1 and control cells. The top panel shows the track of a representative migrating PI3Kγ inhibited cell and the bottom panel, its corresponding volume normalized to the pre-stimulation volume. The scale bar is 50 microns.

 

Reviewer #2 (Public Review):

Nagy et al investigated the role of volume increase and swelling in neutrophils in response to the chemoattractant. Authors show that following chemoattractant response cells lose their volume slightly owing to the cell spreading phase and then have a relatively rapid increase in the cell volume that is concomitant with cell migration. The authors performed an impressive genome-wide CRISPR screen and buoyant density assay to identify the regulators of neutrophil swelling. This assay showed that stimulating cells with chemoattractant fMLP led to an increase in the cell volume that was abrogated with the FPR1 receptor knockout. The screen revealed a cascade that could potentially be involved in cell swelling including NHE1 (sodium-proton antiporter) and PI3K. NHE1 and PI3K are required for chemoattractant-induced swelling in human primary neutrophils. Authors also suggest slightly different functions of NHE1 and PI3K activity where PI3K is also required to maintain chemoattractant-induced cell shape changes. The authors convincingly show that chemoattractant-induced cell swelling is linked to cell migration and NHE1 is required for swelling at the later stages of swelling since the cells at the early point work on low-volume and low-velocity regime. Interestingly, the authors also show that lack of swelling in NHE1-inhibited cells could be rescued by mild hypo-osmotic swelling strengthening the argument that water influx followed chemoattractant stimulation is important for potentiation for migration.

The conclusions of this paper are mostly well supported by data and are pretty convincing, but some aspects of image acquisition and data analysis need to be clarified and extended.

We thank the reviewer for their positive appraisal of our work and pursued their suggestions for improving our paper in this revision.

Weaknesses

(1) It would really help if the authors could add the missing graph for the footprint area when cells are treated with Latranculin. Graph S1F for volume changes with Lat treatment should be compared with DMSO-treated controls.

We agree that the Latrunculin condition merits more thorough investigation. To this end, we compared the volume response of human primary neutrophils to chemoattractant addition for Latrunculin B treated cells versus DMSO controls in suspension and show that there is no difference in swelling (Figure 1 – supplemental figure 2A) . This is additionally confirmed with FxM measurements with a slight undershooting of the final volume likely due to minor uptake of the excluded dye by Latrunculin treated cells (Figure 1 – supplemental figure 2B) . We have also included the requested footprint area changes in the Latrunculin treated cells as compared to controls (Figure 1 – supplemental figure 2C) . The treated cell footprints increase much less than the controls, and this is likely due to a lack of active cell spreading in the Latrunculin treated cells. The increase in footprint area observed following latrunculin treatment is within the range of what would be expected for the 2D projection of an isotropically expanding sphere fitted to the Latrunculin volume data (salmon line).

Author response image 4.

Chemoattractant-induced swelling, but not motility, is independent of actin polymerization. (A) Human primary eutrophils were incubated with DMSO or Latrunculin B, activated with 20 nM fMLP, and then volume responses were measured using electronic sizing via a Coulter counter. Latrunculin treatment did not alter cell swelling, indicating that actin polymerization is dispensable for the chemoattractant-induced volume increase. (B) Similar results were obtained using the FxM assay, showing that Latrunculin-treated cells are capable of swelling after stimulation. (C) The Latrunculin-treated cells also increase their footprints, albeit less so than control cells, but this is within the range of what would be expected for this degree of chemoattractant-induced volume increase (modeled by a sphere expanding an equivalent volume).

(2) The authors show inhibition of NHE1 blocked cell swelling using Coulter counter, a similar experiment should be done with PI3K inhibitions especially since they see PI3K inhibition impact chemoattractant-induced cell shape change.

Good idea. PI3Ky inhibition led to a substantial reduction in the chemoattractant-driven swelling in suspension showing the critical role of PI3K in the swelling of human primary neutrophils (Figure 3 – supplemental figure 1B) .

Author response image 5.

Additional validation of swelling screen hits. (B) To validate the perturbations to cell swelling observed with FxM, primary human neutrophils were stimulated in suspension, and their volumes were measured using a Coulter counter. 20 nM fMLP was added at the 0 minute mark. Shaded regions represent the 95% confidence intervals.

(3) It would be more convincing visually if the authors could also include the movie of cell spreading (footprint) and then mobility with PI3K inhibition.

Included as suggested. We agree this is a more compelling way to present the data (Figure 4 – supplemental figure 1A-D,G)

Author response image 6.

Additional validation of motility phenotypes. (A-D) Single cell tracks of primary human neutrophils responding to acute chemoattractant stimulation. Both panels show tracks of cells 15 minutes prior (left) versus 15 minutes post (right) uncaging the chemoattractant. The scale bar is 50 microns. Color saturation indicates time with tracks progressing from gray to full color. (A) Control cells show a large increase in movement upon uncaging. (D) PI3Kγ leads to a large fraction of cells failing to initiate movement. (E) PI3Kγ inhibition showed near complete blockage of the chemoattractant-induced motility increase in primary human neutrophils. (G) For the PI3Kγ inhibited cells that start migrating, the migration-induced volume fluctuations are comparable to iNHE1 and control cells. The top panel shows the track of a representative migrating PI3Kγ inhibited cell and the bottom panel, its corresponding volume normalized to the pre-stimulation volume. The scale bar is 50 microns.

(4) It is not clear how cell spreading and later volume increase are linked to overall mobility of neutrophils. Are authors suggesting that cell spreading is not required for cell mobility in neutrophils?

We did not mean to imply that cell spreading is not required for neutrophil motility. We take advantage of the fact that we can inhibit cell swelling without inhibiting spreading to investigate the specific role of swelling on migration ( Figure 4) . Conversely, cell spreading on a substrate is not required for chemoattractant-induced cell swelling, as chemoattractant-induced swelling occurs in latrunculin-treated cells (Figure 1 – supplemental figure 2A-C) . However, these latrunculin-treated cells are not able to migrate, at least not in the context studied here (Figure 1 – supplemental figure 2 D-E) . Cell spreading and swelling are likely both critical contributors to neutrophil motility, but their relative importance is dependent on the migratory context. The single cell volume fluctuation analysis indicates that migration-associated spreading and shape changes have large impacts on cell volume ( Figure 1 F) . These fluctuations are asynchronous, obscuring their observation at the population level, but the single cell traces clearly demonstrate them and their correlation with movement.

( 5) Volume fluctuations associated with motility were impacted by NHE1 inhibition at the baselines, what about PI3K inhibitions? Does that impact the actual fluctuations?

PI3K inhibition causes a significant fraction of cells to stop migrating (Figure 4 – supplemental figure 1D) , but among those that do move, they are still able to fluctuate in volume (Figure 4 – supplemental figure 1G) .

Author response image 7.

Additional validation of motility phenotypes. (G) For the PI3Kγ inhibited cells that start migrating, the migration-induced volume fluctuations are comparable to iNHE1 and control cells. The top panel shows the track of a representative migrating PI3Kγ inhibited cell and the bottom panel, its corresponding volume normalized to the pre-stimulation volume. The scale bar is 50 microns.

In contrast, latrunculin abolishes the volume fluctuations that normally accompany migration (Figure 1 – supplemental figure 2F-G) . These data suggest that movement/spreading itself is the driver of the rapid volume fluctuations. In contrast, the sustained volume increase following chemoattractant stimulation is independent of shape change and still occurs in latrunculin-treated cells.

Author response image 8.

Chemoattractant-induced swelling, but not motility, is independent of actin polymerization. (F) Representative single cell volume traces show that Latrunculin-treated cells (black) lack short-term volume fluctuations but persistently maintain an elevated volume following chemoattractant stimulation. Control cells (blue) exhibit short-term volume fluctuations. (G) The lack of short-term volume fluctuations following latrunculin treatment is borne out across the population, with the coefficient of variation in the volume for single cells (post-swelling) being dramatically lower in Latrunculin-treated cells, suggesting that these short term volume fluctuations depend on actin-based motility.

(6) It would really help if the authors compared similar analyses and drew conclusions from that, for example, it is unclear what the authors mean by they found no change in the angular persistence of WT and NHE1 inhibited cells which is in contrast to PI3K inhibition since they do not really have an analysis for angular persistence in PI3K inhibited cells. (S4A and S4B).

Thanks for catching this oversight in these experiments that we previously performed but neglected to include in the initial submission. We now include plots for angular persistence, velocity, and footprint size for the PI3K-gamma-inhibited cells. The results show that PI3K-gamma inhibition interferes both with swelling (Figure 3 – supplemental figure 1B-D) and motility (Figure 4 – supplemental figure 1D-F) , which aligns with its role upstream of the other hits identified in our screen.

Author response image 9.

Additional validation of motility phenotypes. (A-D) Single cell tracks of primary human neutrophils responding to acute chemoattractant stimulation. Both panels show tracks of cells 15 minutes prior (left) versus 15 minutes post (right) uncaging the chemoattractant. The scale bar is 50 microns. Color saturation indicates time with tracks progressing from gray to full color. (A) Control cells show a large increase in movement upon uncaging, (B) NHE1 inhibited cells also initiate movement but to a lesser degree, (C) hypo-osmotic shock rescues the NHE1 motility defect. (D) PI3Kγ leads to a large fraction of cells failing to initiate movement. (E) PI3Kγ inhibition showed near complete blockage of the chemoattractant-induced motility increase in primary human neutrophils. (F) Control neutrophils (blue) show an increased angular alignment upon stimulation as their motility becomes directional. NHE1-inhibition (gold, iNHE1) has very little effect on this process, while PI3Kγ inhibition (green) leads to a reduction in this alignment at the population level. (G) For the PI3Kγ inhibited cells that start migrating, the migration-induced volume fluctuations are comparable to iNHE1 and control cells. The top panel shows the track of a representative migrating PI3Kγ inhibited cell and the bottom panel, its corresponding volume normalized to the pre-stimulation volume. The scale bar is 50 microns.

Author response:

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

eLife assessment

The authors discuss an effect, "diffusive lensing", by which particles would accumulate in high-viscosity regions, for instance in the intracellular medium. To obtain these results, the authors rely on agent-based simulations using custom rules performed with the Ito stochastic calculus convention. The "lensing effect" discussed is a direct consequence of the choice of the Ito convention without spurious drift which has been discussed before and is likely to be inadequate for the intracellular medium, causing the presented results to likely have little relevance for biology.

We thank the editors and the reviewers for their consideration of our manuscript. We argue in this rebuttal and revision that our results and conclusions are in fact likely to have relevance for biology. While we use the Itô convention for ease of modeling considering its non-anticipatory nature upon discretization (see (Volpe and Wehr 2016) for the discretization schemes), we refer to Figure S1B to emphasize that diffusive lensing occurs not only under the Itô convention but across a wide parameter space. Indeed, it is absent only in the normative isothermal convention; note that even a stochastic differential equation conforming to the isothermal convention may be reformulated into the Itô convention by adding suitable drift terms, allowing for diffusive lensing to be seen even in case of the isothermal convention. We note in particular that the choice of the convention is a highly context-dependent one (Sokolov 2010); there is not a universally correct choice, and one can obtain stochastic differential equations consistent with Ito or Stratonovich interpretations in different regimes. Lastly, space-dependent diffusivity is now an experimentally well-recognized feature of the cellular interior, as noted in our references and as discussed further later in this response. This fact points towards the potential relevance of our model for subcellular diffusion.

In our revised preprint, we have made changes to the text and minor changes to figures to address reviewer concerns.

Responses to the Reviewers

We thank the reviewers for their feedback and address the issues they raised in this rebuttal and in the revised manuscript. The central point that the reviewers raise concerns the validity of the drift-less Itô interpretation in modeling potential nonequilibrium types of subcellular transport arising from space-dependent diffusivity. If the drift term were considered, the resulting stochastic differential equation stochastic differential equation (SDE) is equivalent to one arising from the isothermal interpretation of heterogeneous diffusivity (Volpe and Wehr 2016), wherein no diffusive lensing is seen (as shown in Fig. S1B). That is, the isothermal interpretation and the drift-comprising Itô SDE produce the same uniform steady-state particle densities.

While we agree with the reviewers that for a given interpretation, equivalent stochastic differential equations (SDEs) arising from other interpretations may be drawn, we disagree with the generalization that all types of subcellular diffusion conform to the isothermal interpretation. That is, there is no reason why any and all instances of nonequilibrium subcellular particle diffusion must be modeled using isothermal-conforming SDEs (such as the drift-comprising Itô SDE, for instance). We refer to (Sokolov 2010) which prescribes choosing a convention in a context-dependent manner. In this regard, we disagree with the second reviewer’s characterization of making such a choice merely a “choice of writing” considering that it is entirely dependent on the choice of microscopic parameters, as detailed in the discussion section of the manuscript. The following references have also been added to the manuscript: the reference from the first reviewer (Kupferman et al. 2004) proposes a prescription for choosing an appropriate convention based upon comparing the noise correlation time and the particle relaxation time. The reference notes that the Itô convention is appropriate when the particle relaxation time is large when compared to the noise correlation time and the Stratonovich convention is appropriate in the converse scenario. In (Rupprecht et al. 2018), active noise is considered and the resulting Fokker-Planck equation conforms to the Stratonovich convention when thermal noise was negligible. The related reference, (Vishen et al. 2019) compares three timescales: those of particle relaxation, noise correlation and viscoelastic relaxation, to make the choice. Indeed, as noted in the manuscript, lensing is seen in all but one interpretation (without drift additions); only its magnitude is altered by the interpretation/choice of the drift term. The appendix has been modified to include a subsection on the interchangeability of the conventions.

Separately, with regards to the discussion on anomalous diffusion, the section on mean squared displacement calculation has been amended to avoid confusing our model with canonical anomalous diffusion which considers the anomalous exponent; how the anomalous exponent varies with space-dependent diffusivity offers an interesting future area of study.

Responses to specific reviewer comments appear below.

Reviewer #1 (Public Review):

The manuscript "Diffusive lensing as a mechanism of intracellular transport and compartmentalization", explores the implications of heterogeneous viscosity on the diffusive dynamics of particles. The authors analyze three different scenarios:

(i)   diffusion under a gradient of viscosity,

(ii)  clustering of interacting particles in a viscosity gradient, and

(iii) diffusive dynamics of non-interacting particles with circular patches of heterogeneous viscous medium.

The implications of a heterogeneous environment on phase separation and reaction kinetics in cells are under-explored. This makes the general theme of this manuscript very relevant and interesting. However, the analysis in the manuscript is not rigorous, and the claims in the abstract are not supported by the analysis in the main text.

Following are my main comments on the work presented in this manuscript:

(a) The central theme of this work is that spatially varying viscosity leads to position-dependent diffusion constant. This, for an overdamped Langevin dynamics with Gaussian white noise, leads to the well-known issue of the interpretation of the noise term.

The authors use the Ito interpretation of the noise term because their system is non-equilibrium.

One of the main criticisms I have is on this central point. The issue of interpretation arises only when there are ill-posed stochastic dynamics that do not have the relevant timescales required to analyze the noise term properly. Hence, if the authors want to start with an ill-posed equation it should be mentioned at the start. At least the Langevin dynamics considered should be explicitly mentioned in the main text. Since this work claims to be relevant to biological systems, it is also of significance to highlight the motivation for using the ill-posed equation rather than a well-posed equation. The authors refer to the non-equilibrium nature of the dynamics but it is not mentioned what non-equilibrium dynamics to authors have in mind. To properly analyze an overdamped Langevin dynamics a clear source of integrated timescales must be provided. As an example, one can write the dynamics as Eq. (1) \dot x = f(x) + g(x) \eta , which is ill-defined if the noise \eta is delta correlated in time but well-defined when \eta is exponentially correlated in time. One can of course look at the limit in which the exponential correlation goes to a delta correlation which leads to Eq. (1) interpreted in Stratonovich convention. The choice to use the Ito convention for Eq. (1) in this case is not justified.

We thank the reviewer for detailing their concerns with our model’s assumptions. We have addressed them in the common rebuttal.

(b) Generally, the manuscript talks of viscosity gradient but the equations deal with diffusion which is a combination of viscosity, temperature, particle size, and particle-medium interaction. There is no clear motivation provided for focus on viscosity (cytoplasm as such is a complex fluid) instead of just saying position-dependent diffusion constant. Maybe authors should use viscosity only when talking of a context where the existence of a viscosity gradient is established either in a real experiment or in a thought experiment.

The manuscript has been amended to use only “diffusivity” to avoid confusion.

(c) The section "Viscophoresis drives particle accumulation" seems to not have new results. Fig. 1 verifies the numerical code used to obtain the results in the later sections. If that is the case maybe this section can be moved to supplementary or at least it should be clearly stated that this is to establish the correctness of the simulation method. It would also be nice to comment a bit more on the choice of simulation methods with changing hopping sizes instead of, for example, numerically solving stochastic ODE.

The main point of this section and of Fig. 1 is the diffusive lensing effect itself: the accumulation of particles in lower-diffusivity areas. To the best of our knowledge, diffusive lensing has not been reported elsewhere as a specific outcome of non-isothermal interpretations of diffusion, with potential relevance to nonequilibrium subcellular motilities. The simulation method has been fully described in the Methods section, and the code has also been shared (see Code Availability).

A minor comment, the statement "the physically appropriate convention to use depends upon microscopic parameters and timescale hierarchies not captured in a coarse-grained model of diffusion." is not true as is noted in the references that authors mention, a correct coarse-grained model provides a suitable convention (see also Phys. Rev. E, 70(3), 036120., Phys. Rev. E, 100(6), 062602.).

This has been addressed in the common rebuttal.

(d) The section "Interaction-mediated clustering is affected by viscophoresis" makes an interesting statement about the positioning of clusters by a viscous gradient. As a theoretical calculation, the interplay between position-dependent diffusivity and phase separation is indeed interesting, but the problem needs more analysis than that offered in this manuscript. Just a plot showing clustering with and without a gradient of diffusion does not give enough insight into the interplay between density-dependent diffusion and position-dependent diffusion. A phase plot that somehow shows the relative contribution of the two effects would have been nice. Also, it should be emphasized in the main text that the inter-particle interaction is through a density-dependent diffusion constant and not a conservative coupling by an interaction potential.

The density-dependence has been added from the Methods to the main text. The goal of the work is to present lensing as a natural outcome of the parameter choices we make and present its effects as they relate to clustering and commonly used biophysical methods to probe dynamics within cells. A dense sampling of the phase space and how it is altered as a function of diffusivity, and the subsequent interpretation, lie beyond the scope of the present work but offer exciting future directions of study.

(e) The section "In silico microrheology shows that viscophoresis manifests as anomalous diffusion" the authors show that the MSD with and without spatial heterogeneity is different. This is not a surprise - as the underlying equations are different the MSD should be different.

The goal here is to compare and contrast the ways in which homogeneous and heterogeneous diffusion manifest in simulated microrheology measurements. We hope that an altered saturation MSD, as is observed in our simulations, provokes interest in considering lensing while modeling experimental data.

There are various analogies drawn in this section without any justification:

(i) "the saturation MSD was higher than what was seen in the homogeneous diffusion scenario possibly due to particles robustly populating the bulk milieu followed by directed motion into the viscous zone (similar to that of a Brownian ratchet, (Peskin et al., 1993))."

In case of i), the Brownian ratchet is invoked as a model to explain directed accumulation. We have removed this analogy to avoid confusion as it is not delved into further over the course of our work.

(ii) "Note that lensing may cause particle displacements to deviate from a Gaussian distribution, which could explain anomalous behaviors observed both in our simulations and in experiments in cells (Parry et al., 2014)." Since the full trajectory of the particles is available, it can be analyzed to check if this is indeed the case.

This has been addressed in the common rebuttal.

(f) The final section "In silico FRAP in a heterogeneously viscous environment ... " studies the MSD of the particles in a medium with heterogeneous viscous patches which I find the most novel section of the work. As with the section on inter-particle interaction, this needs further analysis.

We thank the reviewer for their appreciation. In presenting these three sections discussing the effects of diffusive lensing, we intend to broadly outline the scope of this phenomenon in influencing a range of behaviors. Exploring the directions further comprise promising future directions of study that lie beyond the scope of this manuscript.

To summarise, as this is a theory paper, just showing MSD or in silico FRAP data is not sufficient. Unlike experiments where one is trying to understand the systems, here one has full access to the dynamics either analytically or in simulation. So just stating that the MSD in heterogeneous and homogeneous environments are not the same is not sufficient. With further analysis, this work can be of theoretical interest. Finally, just as a matter of personal taste, I am not in favor of the analogy with optical lensing. I don't see the connection.

We value the reviewer’s interest in investigating the causes underlying the differences in the MSDs and agree that it represents a promising future area of study. The main point of this section of the manuscript was to make a connection to experimentally measurable quantities.

Reviewer #2 (Public Review):

Summary:

The authors study through theory and simulations the diffusion of microscopic particles and aim to account for the effects of inhomogeneous viscosity and diffusion - in particular regarding the intracellular environment. They propose a mechanism, termed "Diffusive lensing", by which particles are attracted towards high-viscosity regions where they remain trapped. To obtain these results, the authors rely on agent-based simulations using custom rules performed with the Ito stochastic calculus convention, without spurious drift. They acknowledge the fact that this convention does not describe equilibrium systems, and that their results would not hold at equilibrium - and discard these facts by invoking the fact that cells are out-of-equilibrium. Finally, they show some applications of their findings, in particular enhanced clustering in the high-viscosity regions. The authors conclude that as inhomogeneous diffusion is ubiquitous in life, so must their mechanism be, and hence it must be important.

Strengths:

The article is well-written, and clearly intelligible, its hypotheses are stated relatively clearly and the models and mathematical derivations are compatible with these hypotheses.

We thank the reviewer for their appreciation.

Weaknesses:

The main problem of the paper is these hypotheses. Indeed, it all relies on the Ito interpretation of the stochastic integrals. Stochastic conventions are a notoriously tricky business, but they are both mathematically and physically well-understood and do not result in any "dilemma" [some citations in the article, such as (Lau and Lubensky) and (Volpe and Wehr), make an unambiguous resolution of these]. Conventions are not an intrinsic, fixed property of a system, but a choice of writing; however, whenever going from one to another, one must include a "spurious drift" that compensates for the effect of this change - a mathematical subtlety that is entirely omitted in the article: if the drift is zero in one convention, it will thus be non-zero in another in the presence of diffusive gradients. It is well established that for equilibrium systems obeying fluctuation-dissipation, the spurious drift vanishes in the anti-Ito stochastic convention (which is not "anticipatory", contrarily to claims in the article, are the "steps" are local and infinitesimal). This ensures that the diffusion gradients do not induce currents and probability gradients, and thus that the steady-state PDF is the Gibbs measure. This equilibrium case should be seen as the default: a thermal system NOT obeying this law should warrant a strong justification (for instance in the Volpe and Wehr review this can occur through memory effects in robotic dynamics, or through strong fluctuation-dissipation breakdown). In near-equilibrium thermal systems such as the intracellular medium (where, although out-of-equilibrium, temperature remains a relevant and mostly homogeneous quantity), deviations from this behavior must be physically justified and go to zero when going towards equilibrium.

Considering that the physical phenomena underlying diffusion span a range of timescales (particle relaxation, noise, environmental correlation, et cetera), we disagree with the assertion that all types of subcellular diffusion processes can be modeled as occurring at thermal equilibrium: for example, one can easily imagine memory effects arising in the presence of an appropriate hierarchy of timescales. We have added references that describe in more detail the way in which the comparison of timescales can dictate the applicability of different conventions. We also refer the referee to the common rebuttal section of our response in which we discuss factors that govern the choice of the interpretation. The adiabatic elimination arguments highlighted in (Kupferman et al. 2004) provide a clear description of how relevant particle and environment-related timescales can inform the choice of stochastic calculus to use.

With regards to the use of the term “anticipatory” to refer to the isothermal interpretation, we refer to the comment in (Volpe and Wehr 2016) of the Itô interpretation “not looking into the future”. In any case, whether anticipatory or otherwise, the interpretation’s effect on our model remains unchanged, as highlighted in the section in the Appendix on the conversion between different conventions; this section has been added to minimize confusion about the effects of the choice of convention on lensing.

Here, drifts are arbitrarily set to zero in the Ito convention (the exact opposite of the equilibrium anti-Ito), which is the equilibrium equivalent to adding a force (with drift $- grad D$) exactly compensating the spurious drift. If we were to interpret this as a breakdown of detailed balance with inhomogeneous temperature, the "hot" region would be effectively at 4x higher temperature than the cold region (i.e. 1200K) in Fig 1A.

Our work is based on existing observations of space-dependent diffusivity in cells (Garner et al., 2023; Huang et al., 2021; Parry et al., 2014; Śmigiel et al., 2022; Xiang et al., 2020). These papers support a definitive model for the existence of space-dependent diffusivity without invoking space-dependent temperature.

It is the effects of this arbitrary force (exactly compensating the Ito spurious drift) that are studied in the article. The fact that it results in probability gradients is trivial once formulated this way (and in no way is this new - many of the references, for instance, Volpe and Wehr, mention this).

Addressed in the common rebuttal.

Enhanced clustering is also a trivial effect of this probability gradient (the local concentration is increased by this force field, so phase separation can occur). As a side note the "neighbor sensing" scheme to describe interactions is very peculiar and not physically motivated - it violates stochastic thermodynamics laws too, as the detailed balance is apparently not respected.

The neighbor-sensing scheme used here is just one possible model of an effective attractive potential between particles. Other models that lead to density-dependent attraction between particles should also provide qualitatively similar results as ours; this offers an interesting prospect for future research.

Finally, the "anomalous diffusion" discussion is at odds with what the literature on this subject considers anomalous (the exponent does not appear anomalous).

This has been addressed in the common rebuttal, and the relevant part of the manuscript has been modified to avoid confusion.

The authors make no further justification of their choice of convention than the fact that cells are out-of-equilibrium, leaving the feeling that this is a detail. They make mentions of systems (eg glycogen, prebiotic environment) for which (near-)equilibrium physics should mostly prevail, and of fluctuation-dissipation ("Diffusivity varies inversely with viscosity", in the introduction). Yet the "phenomenon" they discuss is entirely reliant on an undiscussed mechanism by which these assumptions would be completely violated (the citations they make for this - Gnesotto '18 and Phillips '12 - are simply discussions of the fact that cells are out-of-equilibrium, not on any consequences on the convention).

Finally, while inhomogeneous diffusion is ubiquitous, the strength of this effect in realistic conditions is not discussed (this would be a significant problem if the effect were real, which it isn't). Gravitational attraction is also an ubiquitous effect, but it is not important for intracellular compartmentalization.

The manuscript text has been supplemented with additional references that detail the ways in which the comparison of timescales can dictate how one can apply different conventions. We refer the reviewer to the common rebuttal section of our response where we detail factors that dictate the choice of the convention to use. As previously noted, the adiabatic elimination arguments highlighted in (Kupferman et al., 2004) provide a prescription for how different timescales are to be considered in deciding the choice of stochastic calculus to use.

With regards to the strength of space-dependent diffusivity in subcellular milieu, various measurements of heterogeneous diffusivity have been made both across different model systems and via different modalities, as cited in our manuscript. (Garner et al. 2023) used single-particle tracking to determine over 100-fold variability in diffusivity within individual S. pombe cells. Single-molecule measurements in (Xiang et al. 2020) and (Śmigiel et al. 2022) reveal an order-of-magnitude variation in tracer diffusion in mammalian cells and multi-fold variation in E. coli cytoplasm respectively. Fluorescence correlation spectroscopy measurements in (Huang et al. 2022) have found a two-fold increase in short-range diffusion of protein-sized tracers in X. laevis extracts. We have also added a reference to a study that uses 3D single particle tracking in the cytosol of a multinucleate fungus, A. gossypii, to identify regions of low-diffusivity near nuclei and hyphal tips (McLaughlin et al. 2020). Many of these references deploy particle tracking and investigate how mesoscale-sized particles (i.e. tracers spanning biologically relevant size scales) are directly impacted by space-dependent diffusivity. Therefore, we base our model on not only space-dependent diffusivity being a well-recognized feature of the cellular interior, but also on these observations pertaining to mesoscale-sized particles’ motion along relevant timescales.

These measurements are also relevant to the reviewer’s question about the strength of the effect, which depends directly on the variability in diffusivity: for ten- or a hundred-fold diffusivity variations, the effect would be expected to be significant. In case of using the Itô convention directly, the contrast in concentration gradient is, in fact, that of the diffusivity gradient.

To conclude, the "diffusive lensing" effect presented here is not a deep physical discovery, but a well-known effect of sticking to the wrong stochastic convention.

As detailed in the various responses above, we respectfully disagree with the notion that there exists a singular correct stochastic convention that is applicable for all cases of subcellular heterogeneous diffusion. Further, as detailed in (Volpe and Wehr 2016) and as detailed in the Appendix, it is possible to convert between conventions and that an isothermal-abiding stochastic differential equation may be suitably altered, by means of adding a drift term, to an Itô-abiding stochastic differential equation; therefore, one can observe diffusive lensing without discarding the isothermal convention if the latter were modified. Indeed, it is only the driftless (or canonical) isothermal convention that does not allow for diffusive lensing.

Author response:

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

Public Review:

This manuscript by Yue et al. aims to understand the molecular mechanisms underlying the better reproductive outcomes of Tibetans at high altitude by characterizing the transcriptome and histology of full-term placenta of Tibetans and compare them to those Han Chinese at high elevations.

The approach is innovative, and the data collected are valuable for testing hypotheses regarding the contribution of the placenta to better reproductive success of populations that adapted to hypoxia. The authors identified hundreds of differentially expressed genes (DEGs) between Tibetans and Han, including the EPAS1 gene that harbors the strongest signals of genetic adaptation. The authors also found that such differential expression is more prevalent and pronounced in the placentas of male fetuses than those of female fetuses, which is particularly interesting, as it echoes with the more severe reduction in birth weight of male neonates at high elevation observed by the same group of researchers (He et al., 2022).

This revised manuscript addressed several concerns raised by reviewers in last round. However, we still find the evidence for natural selection on the identified DEGs--as a group--to be very weak, despite more convincing evidence on a few individual genes, such as EPAS1 and EGLN1.

The authors first examined the overlap between DEGs and genes showing signals of positive selection in Tibetans and evaluated the significance of a larger overlap than expected with a permutation analysis. A minor issue related to this analysis is that the p-value is inflated, as the authors are counting permutation replicates with MORE genes in overlap than observed, yet the more appropriate way is counting replicates with EQUAL or MORE overlapping genes. Using the latter method of p-value calculation, the "sex-combined" and "female-only" DEGs will become non-significantly enriched in genes with evidence of selection, and the signal appears to solely come from male-specific DEGs. A thornier issue with this type of enrichment analysis is whether the condition on placental expression is sufficient, as other genomic or transcriptomic features (e.g., expression level, local sequence divergence level) may also confound the analysis.

According to the suggested methods, we counted the replicates with equal or more overlapping genes than observed (≥4 for the “combined” set; ≥9 for the “male-only” set; ≥0 for the “female-only” set). We found that the overlaps between DEGs and TSNGs were significantly enriched only in the “male-only” set (p-value < 1e-4, counting 0 time from 10,000 permutations), but not in the “female-only” set (p-value = 1, counting 10,000 time from 10,000 permutations), or “combined” set (p-value = 0.0603, counting 603 time from 10,000 permutations) (see Table R1 below).

We updated this information in the revised manuscript, including Results, Methods, and Figure S9.

Author response table 1.

Permutation analysis of the overlapped genes between DEGs and TSNGs.

The authors next aimed to detect polygenic signals of adaptation of gene expression by applying the PolyGraph method to eQTLs of genes expressed in the placenta (Racimo et al 2018). This approach is ambitious but problematic, as the method is designed for testing evidence of selection on single polygenic traits. The expression levels of different genes should be considered as "different traits" with differential impacts on downstream phenotypic traits (such as birth weight). As a result, the eQTLs of different genes cannot be naively aggregated in the calculation of the polygenic score, unless the authors have a specific, oversimplified hypothesis that the expression increase of all genes with identified eQTL will improve pregnancy outcome and that they are equally important to downstream phenotypes. In general, PolyGraph method is inapplicable to eQTL data, especially those of different genes (but see Colbran et al 2023 Genetics for an example where the polygenic score is used for testing selection on the expression of individual genes).

We would recommend removal of these analyses and focus on the discussion of individual genes with more compelling evidence of selection (e.g., EPAS1, EGLN1).

According to the suggestion, we removed these analyses in the revised manuscript.

Author response:

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

Reviewer #1: 

This is my first review of the article entitled "The canonical stopping network: Revisiting the role of the subcortex in response inhibition" by Isherwood and colleagues. This study is one in a series of excellent papers by the Forstmann group focusing on the ability of fMRI to reliably detect activity in small subcortical nuclei - in this case, specifically those purportedly involved in the hyper- and indirect inhibitory basal ganglia pathways. I have been very fond of this work for a long time, beginning with the demonstration of De Hollander, Forstmann et al. (HBM 2017) of the fact that 3T fMRI imaging (as well as many 7T imaging sequences) do not afford sufficient signal to noise ratio to reliably image these small subcortical nuclei. This work has done a lot to reshape my view of seminal past studies of subcortical activity during inhibitory control, including some that have several thousand citations.

In the current study, the authors compiled five datasets that aimed to investigate neural activity associated with stopping an already initiated action, as operationalized in the classic stop-signal paradigm. Three of these datasets are taken from their own 7T investigations, and two are datasets from the Poldrack group, which used 3T fMRI.

The authors make six chief points: 

(1) There does not seem to be a measurable BOLD response in the purportedly critical subcortical areas in contrasts of successful stopping (SS) vs. going (GO), neither across datasets nor within each individual dataset. This includes the STN but also any other areas of the indirect and hyperdirect pathways.

(2) The failed-stop (FS) vs. GO contrast is the only contrast showing substantial differences in those nodes.

(3) The positive findings of STN (and other subcortical) activation during the SS vs. GO contrast could be due to the usage of inappropriate smoothing kernels.

(4) The study demonstrates the utility of aggregating publicly available fMRI data from similar cognitive tasks. 

(5) From the abstract: "The findings challenge previous functional magnetic resonance (fMRI) of the stop-signal task" 

(6) and further: "suggest the need to ascribe a separate function to these networks." 

I strongly and emphatically agree with points 1-5. However, I vehemently disagree with point 6, which appears to be the main thrust of the current paper, based on the discussion, abstract, and - not least - the title.

To me, this paper essentially shows that fMRI is ill-suited to study the subcortex in the specific context of the stop-signal task. That is not just because of the issues of subcortical small-volume SNR (the main topic of this and related works by this outstanding group), but also because of its limited temporal resolution (which is unacknowledged, but especially impactful in the context of the stop-signal task). I'll expand on what I mean in the following.

First, the authors are underrepresenting the non-fMRI evidence in favor of the involvement of the subthalamic nucleus (STN) and the basal ganglia more generally in stopping actions. 

- There are many more intracranial local field potential recording studies that show increased STN LFP (or even single-unit) activity in the SS vs. FS and SS vs. GO contrast than listed, which come from at least seven different labs. Here's a (likely non-exhaustive) list of studies that come to mind:

Ray et al., NeuroImage 2012 <br /> Alegre et al., Experimental Brain Research 2013 <br /> Benis et al., NeuroImage 2014 <br /> Wessel et al., Movement Disorders 2016 <br /> Benis et al., Cortex 2016 <br /> Fischer et al., eLife 2017 <br /> Ghahremani et al., Brain and Language 2018 <br /> Chen et al., Neuron 2020 <br /> Mosher et al., Neuron 2021 <br /> Diesburg et al., eLife 2021 

- Similarly, there is much more evidence than cited that causally influencing STN via deep-brain stimulation also influences action-stopping. Again, the following list is probably incomplete: 

Van den Wildenberg et al., JoCN 2006 <br /> Ray et al., Neuropsychologia 2009 <br /> Hershey et al., Brain 2010 <br /> Swann et al., JNeuro 2011 <br /> Mirabella et al., Cerebral Cortex 2012 <br /> Obeso et al., Exp. Brain Res. 2013 <br /> Georgiev et al., Exp Br Res 2016 <br /> Lofredi et al., Brain 2021 <br /> van den Wildenberg et al, Behav Brain Res 2021 <br /> Wessel et al., Current Biology 2022 

- Moreover, evidence from non-human animals similarly suggests critical STN involvement in action stopping, e.g.: 

Eagle et al., Cerebral Cortex 2008 <br /> Schmidt et al., Nature Neuroscience 2013 <br /> Fife et al., eLife 2017 <br /> Anderson et al., Brain Res 2020 

Together, studies like these provide either causal evidence for STN involvement via direct electrical stimulation of the nucleus or provide direct recordings of its local field potential activity during stopping. This is not to mention the extensive evidence for the involvement of the STN - and the indirect and hyperdirect pathways in general - in motor inhibition more broadly, perhaps best illustrated by their damage leading to (hemi)ballism. 

Hence, I cannot agree with the idea that the current set of findings "suggest the need to ascribe a separate function to these networks", as suggested in the abstract and further explicated in the discussion of the current paper. For this to be the case, we would need to disregard more than a decade's worth of direct recording studies of the STN in favor of a remote measurement of the BOLD response using (provably) sub ideal imaging parameters. There are myriads of explanations of why fMRI may not be able to reveal a potential ground-truth difference in STN activity between the SS and FS/GO conditions, beginning with the simple proposition that it may not afford sufficient SNR, or that perhaps subcortical BOLD is not tightly related to the type of neurophysiological activity that distinguishes these conditions (in the purported case of the stop-signal task, specifically the beta band). But essentially, this paper shows that a specific lens into subcortical activity is likely broken, but then also suggests dismissing existing evidence from superior lenses in favor of the findings from the 'broken' lens. That doesn't make much sense to me.

Second, there is actually another substantial reason why fMRI may indeed be unsuitable to study STN activity, specifically in the stop-signal paradigm: its limited time resolution. The sequence of subcortical processes on each specific trial type in the stop-signal task is purportedly as follows: at baseline, the basal ganglia exert inhibition on the motor system. During motor initiation, this inhibition is lifted via direct pathway innervation. This is when the three trial types start diverging. When actions then have to be rapidly cancelled (SS and FS), cortical regions signal to STN via the hyperdirect pathway that inhibition has to be rapidly reinstated (see Chen, Starr et al., Neuron 2020 for direct evidence for such a monosynaptic hyperdirect pathway, the speed of which directly predicts SSRT). Hence, inhibition is reinstated (too late in the case of FS trials, but early enough in SS trials, see recordings from the BG in Schmidt, Berke et al., Nature Neuroscience 2013; and Diesburg, Wessel et al., eLife 2021). 

Hence, according to this prevailing model, all three trial types involve a sequence of STN activation (initial inhibition), STN deactivation (disinhibition during GO), and STN reactivation (reinstantiation of inhibition during the response via the hyperdirect pathway on SS/FS trials, reinstantiation of inhibition via the indirect pathway after the response on GO trials). What distinguishes the trial types during this period is chiefly the relative timing of the inhibitory process (earliest on SS trials, slightly later on FS trials, latest on GO trials). However, these temporal differences play out on a level of hundreds of milliseconds, and in all three cases, processing concludes well under a second overall. To fMRI, given its limited time resolution, these activations are bound to look quite similar. 

Lastly, further building on this logic, it's not surprising that FS trials yield increased activity compared to SS and GO trials. That's because FS trials are errors, which are known to activate the STN (Cavanagh et al., JoCN 2014; Siegert et al. Cortex 2014) and afford additional inhibition of the motor system after their occurrence (Guan et al., JNeuro 2022). Again, fMRI will likely conflate this activity with the abovementioned sequence, resulting in a summation of activity and the highest level of BOLD for FS trials. 

In sum, I believe this study has a lot of merit in demonstrating that fMRI is ill-suited to study the subcortex during the SST, but I cannot agree that it warrants any reappreciation of the subcortex's role in stopping, which are not chiefly based on fMRI evidence. 

We would like to thank reviewer 1 for their insightful and helpful comments. We have responded point-by-point below and will give an overview of how we reframed the paper here.  

We agree that there is good evidence from other sources for the presence of the canonical stopping network (indirect and hyperdirect) during action cancellation, and that this should be reflected more in the paper. However, we do not believe that a lack of evidence for this network during the SST makes fMRI ill-suited for studying this task, or other tasks that have neural processes occurring in quick succession. What we believe the activation patterns of fMRI reflect during this task, is the large of amount of activation caused by failed stops. That is, that the role of the STN in error processing may be more pronounced that its role in action cancellation. Due to the replicability of fMRI results, especially at higher field strengths, we believe the activation profile of failed stop trials reflects a paramount role for the STN in error processing. Therefore, while we agree we do not provide evidence against the role of the STN in action cancellation, we do provide evidence that our outlook on subcortical activation during different trial types of this task should be revisited. We have reframed the article to reflect this, and discuss points such as fMRI reliability, validity and the complex overlapping of cognitive processes in the SST in the discussion. Please see all changes to the article indicated by red text.

A few other points: 

- As I said before, this team's previous work has done a lot to convince me that 3T fMRI is unsuitable to study the STN. As such, it would have been nice to see a combination of the subsamples of the study that DID use imaging protocols and field strengths suitable to actually study this node. This is especially true since the second 3T sample (and arguably, the Isherwood_7T sample) does not afford a lot of trials per subject, to begin with.

Unfortunately, this study already comprises of the only 7T open access datasets available for the SST. Therefore, unless we combined only the deHollander_7T and Miletic_7T subsamples there is no additional analysis we can do for this right now. While looking at just the sub samples that were 7T and had >300 trials would be interesting, based on the new framing of the paper we do not believe it adds to the study, as the sub samples still lack the temporal resolution seemingly required for looking at the processes in the SST.

- What was the GLM analysis time-locked to on SS and FS trials? The stop-signal or the GO-signal? 

SS and FS trials were time-locked to the GO signal as this is standard practice. The main reason for this is that we use contrasts to interpret differences in activation patterns between conditions. By time-locking the FS and SS trials to the stop signal, we are contrasting events at different time points, and therefore different stages of processing, which introduces its own sources of error. We agree with the reviewer, however, that a separate analysis with time-locking on the stop-signal has its own merit, and now include results in the supplementary material where the FS and SS trials are time-locked to the stop signal as well.

- Why was SSRT calculated using the outdated mean method? 

We originally calculated SSRT using the mean method as this was how it was reported in the oldest of the aggregated studies. We have now re-calculated the SSRTs using the integration method with go omission replacement and thank the reviewer for pointing this out. Please see response to comment 3.

- The authors chose 3.1 as a z-score to "ensure conservatism", but since they are essentially trying to prove the null hypothesis that there is no increased STN activity on SS trials, I would suggest erring on the side of a more lenient threshold to avoid type-2 error. 

We have used minimum FDR-corrected thresholds for each contrast now, instead of using a blanket conservative threshold of 3.1 over all contrasts. The new thresholds for each contrast are shown in text. Please see below (page 12):

“The thresholds for each contrast are as follows: 3.01 for FS > GO, 2.26 for FS > SS and 3.1 for SS > GO.”

- The authors state that "The results presented here add to a growing literature exposing inconsistencies in our understanding of the networks underlying successful response inhibition". It would be helpful if the authors cited these studies and what those inconsistencies are. 

We thank reviewer 1 for their detailed and thorough evaluation of our paper. Overall, we agree that there is substantial direct and indirect evidence for the involvement of the cortico-basal-ganglia pathways in response inhibition. We have taken the vast constructive criticism on board and agree with the reviewer that the paper should be reframed. We would like to thank the reviewer for the thoroughness of their helpful comments aiding the revising of the paper.

(1) I would suggest reframing the study, abstract, discussion, and title to reflect the fact that the study shows that fMRI is unsuitable to study subcortical activity in the SST, rather than the fact that we need to question the subcortical model of inhibition, given the reasons in my public review.

We agree with the reviewer that the article should be reframed and not taken as direct evidence against the large sum of literature pointing towards the involvement of the cortico-basal-ganglia pathway in response inhibition. We have significantly rewritten the article in light of this.

(2) I suggest combining the datasets that provide the best imaging parameters and then analyzing the subcortical ROIs with a more lenient threshold and with regressors time-locked to the stop-signals (if that's not already the case). This would make the claim of a null finding much more impactful. Some sort of power analysis and/or Bayes factor analysis of evidence for the null would also be appreciated. 

Instead of using a blanket conservative threshold of 3.1, we instead used only FDR-corrected thresholds. The threshold level is therefore different for each contrast and noted in the figures. We have also added supplementary figures including the group-level SPMs and ROI analyses when the FS and SS trials were time-locked to the stop signal instead of the GO signal (Supplementary Figs 4 & 5). But as mentioned above, due to the difference in time points when contrasting, we believe that time-locking to the GO signal for all trial types makes more sense for the main analysis.

We have now also computed BFs on the first level ROI beta estimates for all contrasts using the BayesFactor package as implemented in R. We add the following section to the methods and updated the results section accordingly (page 8):

“In addition to the frequentist analysis we also opted to compute Bayes Factors (BFs) for each contrast per ROI per hemisphere. To do this, we extracted the beta weights for each individual trial type from our first level model. We then compared the beta weights from each trial type to one another using the ‘BayesFactor’ package as implement in R (Morey & Rouder, 2015). We compared the full model comprising of trial type, dataset and subject as predictors to the null model comprising of only the dataset and subject as predictor. The datasets and subjects were modeled as random factors. We divided the resultant BFs from the full model by the null model to provide evidence for or against a significant difference in beta weights for each trial type. To interpret the BFs, we used a modified version of Jeffreys’ scale (Jeffreys, 1939; Lee & Wagenmakers, 2014).”

(3) I suggest calculating SSRT using the integration method with the replacement of Go omissions, as per the most recent recommendation (Verbruggen et al., eLife 2019).

We agree we should have used a more optimal method for SSRT estimation. We have replaced our original estimations with that of the integration method with go omissions replacement, as suggested and adapted the results in table 3.

We have also replaced text in the methods sections to reflect this (page 5):

“For each participant, the SSRT was calculated using the mean method, estimated by subtracting the mean SSD from median go RT (Aron & Poldrack, 2006; Logan & Cowan, 1984).”

Now reads:

“For each participant, the SSRT was calculated using the integration method with replacement of go omissions (Verbruggen et al., 2019), estimated by integrating the RT distribution and calculating the point at which the integral equals p(respond|signal). The completion time of the stop process aligns with the nth RT, where n equals the number of RTs in the RT distribution of go trials multiplied by the probability of responding to a signal.”

Reviewer #2:

This work aggregates data across 5 openly available stopping studies (3 at 7 tesla and 2 at 3 tesla) to evaluate activity patterns across the common contrasts of Failed Stop (FS) > Go, FS > stop success (SS), and SS > Go. Previous work has implicated a set of regions that tend to be positively active in one or more of these contrasts, including the bilateral inferior frontal gyrus, preSMA, and multiple basal ganglia structures. However, the authors argue that upon closer examination, many previous papers have not found subcortical structures to be more active on SS than FS trials, bringing into question whether they play an essential role in (successful) inhibition. In order to evaluate this with more data and power, the authors aggregate across five datasets and find many areas that are *more* active for FS than SS, specifically bilateral preSMA, caudate, GPE, thalamus, and VTA, and unilateral M1, GPi, putamen, SN, and STN. They argue that this brings into question the role of these areas in inhibition, based upon the assumption that areas involved in inhibition should be more active on successful stop than failed stop trials, not the opposite as they observed. 

As an empirical result, I believe that the results are robust, but this work does not attempt a new theoretical synthesis of the neuro-cognitive mechanisms of stopping. Specifically, if these many areas are more active on failed stop than successful stop trials, and (at least some of) these areas are situated in pathways that are traditionally assumed to instantiate response inhibition like the hyperdirect pathway, then what function are these areas/pathways involved in? I believe that this work would make a larger impact if the author endeavored to synthesize these results into some kind of theoretical framework for how stopping is instantiated in the brain, even if that framework may be preliminary. 

I also have one main concern about the analysis. The authors use the mean method for computing SSRT, but this has been shown to be more susceptible to distortion from RT slowing (Verbruggen, Chambers & Logan, 2013 Psych Sci), and goes against the consensus recommendation of using the integration with replacement method (Verbruggen et al., 2019). Therefore, I would strongly recommend replacing all mean SSRT estimates with estimates using the integration with replacement method. 

I found the paper clearly written and empirically strong. As I mentioned in the public review, I believe that the main shortcoming is the lack of theoretical synthesis. I would encourage the authors to attempt to synthesize these results into some form of theoretical explanation. I would also encourage replacing the mean method with the integration with replacement method for computing SSRT. I also have the following specific comments and suggestions (in the approximate order in which they appear in the manuscript) that I hope can improve the manuscript: 

We would like to thank reviewer 2 for their insightful and interesting comments. We have adapted our paper to reflect these comments. Please see direct responses to your comments below. We agree with the reviewer that some type of theoretical synthesis would help with the interpretability of the article. We have substantially reworked the discussion and included theoretical considerations behind the newer narrative. Please see all changes to the article indicated by red text.

(1) The authors say "performance on successful stop trials is quantified by the stop signal reaction time". I don't think this is technically accurate. SSRT is a measure of the average latency of the stop process for all trials, not just for the trials in which subjects successfully stop. 

Thank you for pointing this technically incorrect statement. We have replaced the above sentence with the following (page 1):

“Inhibition performance in the SST as a whole is quantified by the stop signal reaction time (SSRT), which estimates the speed of the latent stopping process (Verbruggen et al., 2019).”

(2) The authors say "few studies have detected differences in the BOLD response between FS and SS trials", but then do not cite any papers that detected differences until several sentences later (de Hollander et al., 2017; Isherwood et al., 2023; Miletic et al., 2020). If these are the only ones, and they only show greater FS than SS, then I think this point could be made more clearly and directly. 

We have moved the citations to the correct place in the text to be clearer. We have also rephrased this part of the introduction to make the points more direct (page 2).

“In the subcortex, functional evidence is relatively inconsistent. Some studies have found an increase in BOLD response in the STN in SS > GO contrasts (Aron & Poldrack, 2006; Coxon et al., 2016; Gaillard et al., 2020; Yoon et al., 2019), but others have failed to replicate this (Bloemendaal et al., 2016; Boehler et al., 2010; Chang et al., 2020; B. Xu et al., 2015). Moreover, some studies have actually found higher STN, SN and thalamic activation in failed stop trials, not successful ones (de Hollander et al., 2017; Isherwood et al., 2023; Miletić et al., 2020).”

(3) Unless I overlooked it, I don't believe that the author specified the criterion that any given subject is excluded based upon. Given some studies have significant exclusions (e.g., Poldrack_3T), I think being clear about how many subjects violated each criterion would be useful. 

This is indeed interesting and important information to include. We have added the number of participants who were excluded for each criterion. Please see added text below (page 4):

“Based on these criteria, no subjects were excluded from the Aron_3T dataset. 24 subjects were excluded from the Poldrack_3T dataset (3 based on criterion 1, 9 on criterion 2, 11 on criterion 3, and 8 on criterion 4). Three subjects were excluded from the deHollander_7T dataset (2 based on criterion 1 and 1 on criterion 2). Five subjects were excluded from the Isherwood_7T dataset (2 based on criterion 1, 1 on criterion 2, and 2 on criterion 4). Two subjects were excluded from the Miletic_7T dataset (1 based on criterion 2 and 1 on criterion 4). Note that some participants in the Poldrack_3T study failed to meet multiple inclusion criteria.”

(4) The Method section included very exhaustive descriptions of the neuroimaging processing pipeline, which was appreciated. However, it seems that much of what is presented is not actually used in any of the analyses. For example, it seems that "functional data preprocessing" section may be fMRIPrep boilerplate, which again is fine, but I think it would help to clarify that much of the preprocessing was not used in any part of the analysis pipeline for any results. For example, at first blush, I thought the authors were using global signal regression, but after a more careful examination, I believe that they are only computing global signals but never using them. Similarly with tCompCor seemingly being computed but not used. If possible, I would recommend that the authors share code that instantiates their behavioral and neuroimaging analysis pipeline so that any confusion about what was actually done could be programmatically verified. At a minimum, I would recommend more clearly distinguishing the pipeline steps that actually went into any presented analyses.

We thank the reviewer for finding this inconsistency. The methods section indeed uses the fMRIprep boilerplate text, which we included so to be as accurate as possible when describing the preprocessing steps taken. While we believe leaving the exact boilerplate text that fMRIprep gives us is the most accurate method to show our preprocessing, we have adapted some of the text to clarify which computations were not used in the subsequent analysis. As a side-note, for future reference, we’d like to add that the fmriprep authors expressly recommend users to report the boilerplate completely and unaltered, and as such, we believe this may become a recurring issue (page 7).

“While many regressors were computed in the preprocessing of the fMRI data, not all were used in the subsequent analysis. The exact regressors used for the analysis can be found above. For example, tCompCor and global signals were calculated in our generic preprocessing pipeline but not part of the analysis. The code used for preprocessing and analysis can be found in the data and code availability statement.”

(5) What does it mean for the Poldrack_3T to have N/A for SSD range? Please clarify. 

Thank you for pointing out this omission. We had not yet found the possible SSD range for this study. We have replaced this value with the correct value (0 – 1000 ms).

(6) The SSD range of 0-2000ms for deHollander_7T and Miletic_7T seems very high. Was this limit ever reached or even approached? SSD distributions could be a useful addition to the supplement. 

Thank you for also bringing this mistake to light. We had accidentally placed the max trial duration in these fields instead of the max allowable SSD value. We have replaced the correct value (0 – 900 ms).

(7) The author says "In addition, median go RTs did not correlate with mean SSRTs within datasets (Aron_3T: r = .411, p = .10, BF = 1.41; Poldrack_3T: r = .011, p = .91, BF = .23; deHollander_7T: r = -.30, p = .09, BF = 1.30; Isherwood_7T: r = .13, p = .65, BF = .57; Miletic_7T: r = .37, p = .19, BF = 1.02), indicating independence between the stop and go processes, an important assumption of the horse-race model (Logan & Cowan, 1984)." However, the independent race model assumes context independence (the finishing time of the go process is not affected by the presence of the stop process) and stochastic independence (the duration of the go and stop processes are independent on a given trial). This analysis does not seem to evaluate either of these forms of independence, as it correlates RT and SSRT across subjects, so it was unclear how this analysis evaluated either of the types of independence that are assumed by the independent race model. Please clarify or remove. 

Thank you for this comment. We realize that this analysis indeed does not evaluate either context or stochastic independence and therefore we have removed this from the manuscript.

(8) The RTs in Isherwood_7T are considerably slower than the other studies, even though the go stimulus+response is the same (very simple) stimulus-response mapping from arrows to button presses. Is there any difference in procedure or stimuli that might explain this difference? It is the only study with a visual stop signal, but to my knowledge, there is no work suggesting visual stop signals encourage more proactive slowing. If possible, I think a brief discussion of the unusually slow RTs in Isherwood_7T would be useful. 

We have included the following text in the manuscript to reflect this observed difference in RT between the Isherwood_7T dataset and the other datasets (page 9).

“Longer RTs were found in the Isherwood_7T dataset in comparison to the four other datasets. The only difference in procedure in the Isherwood_7T dataset is the use of a visual stop signal as opposed to an auditory stop signal. This RT difference is consistent with previous research, where auditory stop signals and visual go stimuli have been associated with faster RTs compared to unimodal visual presentation (Carrillo-de-la-Peña et al., 2019; Weber et al., 2024). The mean SSRTs and probability of stopping are within normal range, indicating that participants understood the task and responded in the expected manner.”

(9) When the authors included both 3T and 7T data, I thought they were preparing to evaluate the effect of magnet strength on stop networks, but they didn't do this analysis. Is this because the authors believe there is insufficient power? It seems that this could be an interesting exploratory analysis that could improve the paper.

We thank the reviewer for this interesting comment. As our dataset sample contains only two 3T and three 7T datasets we indeed believe there is insufficient power to warrant such an analysis. In addition, we wanted the focus of this paper to be how fMRI examines the SST in general, and not differences between acquisition methods. With a greater number of datasets with different imaging parameters (especially TE or resolution) in addition to field strength, we agree such an analysis would be interesting, although beyond the scope of this article.

(10) The authors evaluate smoothing and it seems that the conclusion that they want to come to is that with a larger smoothing kernel, the results in the stop networks bleed into surrounding areas, producing false positive activity. However, in the absence of a ground truth of the true contributions of these areas, it seems that an alternative interpretation of the results is that the denser maps when using a larger smoothing kernel could be closer to "true" activation, with the maps using a smaller smoothing kernel missing some true activity. It seems worth entertaining these two possible interpretations for the smoothing results unless there is clear reason to conclude that the smoothed results are producing false positive activity. 

We agree with the view of the reviewer on the interpretation of the smoothing results. We indeed cannot rule this out as a possible interpretation of the results, due to a lack of ground truth. We have added text to the article to reflect this view and discuss the types of errors we can expect for both smaller and larger smoothing kernels (page 15).

“In the absence of a ground truth, we are not able to fully justify the use of either larger or smaller kernels to analyse such data. On the one hand, aberrantly large smoothing kernels could lead to false positives in activation profiles, due to bleeding of observed activation into surrounding tissues. On the other side, too little smoothing could lead to false negatives, missing some true activity in surrounding regions. While we cannot concretely validate either choice, it should be noted that there is lower spatial uncertainty in the subcortex compared to the cortex, due to the lower anatomical variability. False positives from smoothing spatially unmatched signal, are more likely than false negatives. It may be more prudent for studies to use a range of smoothing kernels, to assess the robustness of their fMRI activation profiles.”

Author response:

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

General response:

We thank all the reviewers for their detailed reviews.

All reviewers made a number of valuable comments, in particular by highlighting several points that would benefit from additional clarifications and discussion. We really appreciate the time and effort that went into the reviews. We have updated the paper to reflect the changes we have made in response to the reviewers' comments (largely by including more discussion regarding the model limitations and the effect of various modeling choices). We have also included several new supplementary figures (S7, S8, S9, S10) that provide further details of the model behavior, and show the effect of changing some of the terms in the cost. Below, we go through the individual comments, and highlight the places in which we have made changes to address the reviewers’ comments.

Reviewer 1:

Thank you for your review and pointing out multiple things to be discussed and clarified! Below, we go through the various limitations you pointed out and refer to the places where we have tried to address them.

(1) It's important to keep in mind that this work involves simplified models of the motor system, and often the terminology for 'motor cortex' and 'models of motor cortex' are used interchangeably, which may mislead some readers. Similarly, the introduction fails in many cases to state what model system is being discussed (e.g. line 14, line 29, line 31), even though these span humans, monkeys, mice, and simulations, which all differ in crucial ways that cannot always be lumped together.

That is a good point. We have clarified this in the text (Introduction and Discussion), to highlight the fact that our model isn’t necessarily meant to just capture M1. We have also updated the introduction to make it more clear which species the experiments which motivate our investigation were performed in.

(2) At multiple points in the manuscript thalamic inputs during movement (in mice) is used as a motivation for examining the role of preparation. However, there are other more salient motivations, such as delayed sensory feedback from the limb and vision arriving in the motor cortex, as well as ongoing control signals from other areas such as the premotor cortex.

Yes – the motivation for thalamic inputs came from the fact that those have specifically been shown to be necessary for accurate movement generation in mice. However, it is true that the inputs in our model are meant to capture any signals external to the dynamical system modeled, and as such are likely to represent a mixture of sensory signals, and feedback from other areas. We have clarified this in the Discussion, and have added this additional motivation in the Introduction.

(3) Describing the main task in this work as a delayed reaching task is not justified without caveats (by the authors' own admission: line 687), since each network is optimized with a fixed delay period length. Although this is mentioned to the reader, it's not clear enough that the dynamics observed during the delay period will not resemble those in the motor cortex for typical delayed reaching tasks.

Yes, we completely agree that the terminology might be confusing. While the task we are modeling is a delayed reaching task, it does differ from the usual setting since the network has knowledge of the delay period, and that is indeed a caveat of the model. We have added a brief paragraph just after the description of the optimal control objective to highlight this limitation.

We have also performed additional simulations using two different variants of a model-predictive control approach that allow us to relax the assumption that the go-cue time is known in advance. We show that these modifications of the optimal controller yield results that remain consistent with our main conclusions, and can in fact in some settings lead to preparatory activity plateaus during the preparation epoch as often found in monkey M1 (e.g in Elsayed et al. 2016). We have modified the Discussion to explain these results and their limitations, which are summarized in a new Supplementary Figure (S9).

(4) A number of simplifications in the model may have crucial consequences for interpretation.

a) Even following the toy examples in Figure 4, all the models in Figure 5 are linear, which may limit the generalisability of the findings.

While we agree that linear models may be too simplistic, much prior analyses of M1 data suggest that it is often good enough to capture key aspects of M1 dynamics; for example, the generative model underlying jPCA is linear, and Sussillo et al. (2015) showed that the internal activity of nonlinear RNN models trained to reproduce EMG data aligned best with M1 activity when heavily regularized; in this regime, the RNN dynamics were close to linear. Nevertheless, this linearity assumption is indeed convenient from a modeling viewpoint: the optimal control problem is more easily solved for linear network dynamics and the optimal trajectories are more consistent across networks. Indeed, we had originally attempted to perform the analyses of Figure 5 in the nonlinear setting, but found that while the results were overall similar to what we report in the linear regime, iLQR was occasionally trapped into local minimal, resulting in more variable results especially for inhibition-stabilized network in the strongly connected end of the spectrum. Finally, Figure 5 is primarily meant to explore to what extent motor preparation can be predicted from basic linear control-theoretic properties of the Jacobian of the dynamics; in this regard, it made sense to work with linear RNNs (for which the Jacobian is constant).

b) Crucially, there is no delayed sensory feedback in the model from the plant. Although this simplification is in some ways a strength, this decision allows networks to avoid having to deal with delayed feedback, which is a known component of closed-loop motor control and of motor cortex inputs and will have a large impact on the control policy.

This comment resonates well with Reviewer 3's remark regarding the autonomous nature (or not) of M1 during movement. Rather than thinking of our RNN models as anatomically confined models of M1 alone, we think of them as models of the dynamics which M1 implements possibly as part of a broader network involving “inter-area loops and (at some latency) sensory feedback”, and whose state appears to be near-fully decodable from M1 activity alone. We have added a paragraph of Discussion on this important point.

(5) A key feature determining the usefulness of preparation is the direction of the readout dimension. However, all readouts had a similar structure (random Gaussian initialization). Therefore, it would be useful to have more discussion regarding how the structure of the output connectivity would affect preparation, since the motor cortex certainly does not follow this output scheme.

We agree with this limitation of our model — indeed one key message of Figure 4 is that the degree of reliance on preparatory inputs depends strongly on how the dynamics align with the readout. However, this strong dependence is somewhat specific to low-dimensional models; in higher-dimensional models (most of our paper), one expects that any random readout matrix C will pick out activity dimensions in the RNN that are sufficiently aligned with the most controllable directions of the dynamics to encourage preparation.

We did consider optimizing C away (which required differentiating through the iLQR optimizer, which is possible but very costly), but the question inevitably arises what exactly should C be optimized for, and under what constraints (e.g fixed norm or not). One possibility is to optimize C with respect to the same control objective that the control inputs are optimized for, and constrain its norm (otherwise, inputs to the M1 model, and its internal activity, could become arbitrarily small as C can grow to compensate). We performed this experiment (new Supplementary Figure S7) and obtained a similar preparation index; there was one notable difference, namely that the optimized readout modes led to greater observability compared to a random readout; thus, the same amount of “muscle energy” required for a given movement could now be produced by a smaller initial condition. In turn, this led to smaller control inputs, consistent with a lower control cost overall.

Whilst we could have systematically optimized C away, we reasoned that (i) it is computationally expensive, and (ii) the way M1 affects downstream effectors is presumably “optimized” for much richer motor tasks than simple 2D reaching, such that optimizing C for a fixed set of simple reaches could lead to misleading conclusions. We therefore decided to stick with random readouts.

Additional comments :

(1) The choice of cost function seems very important. Is it? For example, penalising the square of u(t) may produce very different results than penalising the absolute value.

Yes, the choice of cost function does affect the results, at least qualitatively. The absolute value of the inputs is a challenging cost to use, as iLQR relies on a local quadratic approximation of the cost function. However, we have included additional experiments in which we penalized the squared derivative of the inputs (Supplementary Figure S8; see also our response to Reviewer 3's suggestion on this topic), and we do see differences in the qualitative behavior of the model (though the main takeaway, i.e. the reliance on preparation, continues to hold). This is now referred to and discussed in the Discussion section.

(2) In future work it would be useful to consider the role of spinal networks, which are known to contribute to preparation in some cases (e.g. Prut and Fetz, 1999).

(3) The control signal magnitude is penalised, but not the output torque magnitude, which highlights the fact that control in the model is quite different from muscle control, where co-contraction would be a possibility and therefore a penalty of muscle activation would be necessary. Future work should consider the role of these differences in control policy.

Thank you for pointing us to this reference! Regarding both of these concerns, we agree that the model could be greatly improved and made more realistic in future work (another avenue for this would be to consider a more realistic biophysical model, e.g. using the MotorNet library). We hope that the current Discussion, which highlights the various limitations of our modeling choices, makes it clear that a lot of these choices could easily be modified depending on the specific assumptions/investigation being performed.

Reviewer 2:

Thank you for your positive review! We very much agree with the limitations you pointed out, some of which overlapped with the comments of the other reviewers. We have done our best to address them through additional discussion and new supplementary figures. We briefly highlight below where those changes can be found.

(1) Though the optimal control theory framework is ideal to determine inputs that minimize output error while regularizing the input norm, it however cannot easily account for some other varied types of objectives especially those that may lead to a complex optimization landscape. For instance, the reusability of parts of the circuit, sparse use of additional neurons when learning many movements, and ease of planning (especially under uncertainty about when to start the movement), may be alternative or additional reasons that could help explain the preparatory activity observed in the brain. It is interesting to note that inputs that optimize the objective chosen by the authors arguably lead to a trade-off in terms of other desirable objectives. Specifically, the inputs the authors derive are time-dependent, so a recurrent network would be needed to produce them and it may not be easy to interpolate between them to drive new movement variants. In addition, these inputs depend on the desired time of output and therefore make it difficult to plan, e.g. in circumstances when timing should be decided depending on sensory signals. Finally, these inputs are specific to the full movement chain that will unfold, so they do not permit reuse of the inputs e.g. in movement sequences of different orders.

Yes, that is a good point! We have incorporated further Discussion related to this point. We have additionally included a new example in which we regularize the temporal complexity of the inputs (see also our response to Reviewer 3's suggestion on this topic), which leads to more slowly varying inputs, and may indeed represent a more realistic constraint and lead to simpler inputs that can more easily be interpolated between. We also agree that uncertainty about the upcoming go cue may play an important role in the strategy adopted by the animals. While we have not performed an extensive investigation of the topic, we have included a Supplementary Figure (S9) in which we used Model Predictive Control to investigate the effect of planning under uncertainty about the go cue arrival time. We hope that this will give the reader a better sense of what sort of model extensions are possible within our framework.

(2) Relatedly, if the motor circuits were to balance different types of objectives, the activity and inputs occurring before each movement may be broken down into different categories that may each specialize into one objective. For instance, previous work (Kaufman et al. eNeuron 2016, Iganaki et al., Cell 2022, Zimnik and Churchland, Nature Neuroscience 2021) has suggested that inputs occurring before the movement could be broken down into preparatory inputs 'stricto sensu' - relating to the planned characteristics of the movement - and a trigger signal, relating to the transition from planning to execution - irrespective of whether the movement is internally timed or triggered by an external event. The current work does not address which type(s) of early input may be labeled as 'preparatory' or may be thought of as a part of 'planning' computations.

Yes, our model does indeed treat inputs in a very general way, and does not distinguish between the different types of processes they may be composed of. This is partly because we do not explicitly model where the inputs come from, such that our inputs likely englobe multiple processes. We have added discussion related to this point.

(3) While the authors rightly point out some similarities between the inputs that they derive and observed preparatory activity in the brain, notably during motor sequences, there are also some differences. For instance, while both the derived inputs and the data show two peaks during sequences, the data reproduced from Zimnik and Churchland show preparatory inputs that have a very asymmetric shape that really plummets before the start of the next movement, whereas the derived inputs have larger amplitude during the movement period - especially for the second movement of the sequence. In addition, the data show trigger-like signals before each of the two reaches. Finally, while the data show a very high correlation between the pattern of preparatory activity of the second reach in the double reach and compound reach conditions, the derived inputs appear to be more different between the two conditions. Note that the data would be consistent with separate planning of the two reaches even in the compound reach condition, as well as the re-use of the preparatory input between the compound and double reach conditions. Therefore, different motor sequence datasets - notably, those that would show even more coarticulation between submovements - may be more promising to find a tight match between the data and the author's inputs. Further analyses in these datasets could help determine whether the coarticulation could be due to simple filtering by the circuits and muscles downstream of M1, planning of movements with adjusted curvature to mitigate the work performed by the muscles while permitting some amount of re-use across different sequences, or - as suggested by the authors - inputs fully tailored to one specific movement sequence that maximize accuracy and minimize the M1 input magnitude.

Regarding the exact shape of the occupancy plots, it is important to note that some of the more qualitative aspects (e.g the relative height of the two peaks) will change if we change the parameters of the cost function. Right now, we have chosen the parameters to ensure that both reaches would be performed at roughly the same speed (as a way to very loosely constrain the parameters based on the observed behavior). However, small changes to the hyperparameters can lead to changes in the model output (e.g one of the two consecutive reaches being performed using greater acceleration than the other), and since our biophysical model is fairly simple, changes in the behavior are directly reflected in the network activity. Essentially, what this means is that while the double occupancy is a consistent feature of the model, the exact shape of the peaks is more sensitive to hyperparameters, and we do not wish to draw any strong conclusions from them, given the simplicity of the biophysical model. However, we do agree that our model exhibits some differences with the data. As discussed above, we have included additional discussion regarding the potential existence of separate inputs for planning vs triggering the movement in the context of single reaches.

Overall, we are excited about the suggestions made by the Reviewer here about using our approach to analyze other motor sequence datasets, but we think that in order to do this properly, one would need to adopt a more realistic musculo-skeletal model (such as one provided by MotorNet).

(4) Though iLQR is a powerful optimization method to find inputs optimizing the author's cost function, it also has some limitations. First, given that it relies on a linearization of the dynamics at each timestep, it has a limited ability to leverage potential advantages of nonlinearities in the dynamics. Second, the iLQR algorithm is not a biologically plausible learning rule and therefore it might be difficult for the brain to learn to produce the inputs that it finds. It remains unclear whether using alternative algorithms with different limitations - for instance, using variants of BPTT to train a separate RNN to produce the inputs in question - could impact some of the results.

We agree that our choice of iLQR has limitations: while it offers the advantage of convergence guarantees, it does indeed restrict the choice of cost function and dynamics that we can use. We have now included extensive discussion of how the modeling choices affect our results.

We do not view the lack of biological plausibility of iLQR as an issue, as the results are agnostic to the algorithm used for optimization. However, we agree that any structure imposed on the inputs (e.g by enforcing them to be the output of a self-contained dynamical system) would likely alter the results. A potentially interesting extension of our model would be to do just what the reviewer suggested, and try to learn a network that can generate the optimal inputs. However, this is outside the scope of our investigation, as it would then lead to new questions (e.g what brain region would that other RNN represent?).

(5) Under the objective considered by the authors, the amount of input occurring before the movement might be impacted by the presence of online sensory signals for closed-loop control. It is therefore an open question whether the objective and network characteristics suggested by the authors could also explain the presence of preparatory activity before e.g. grasping movements that are thought to be more sensory-driven (Meirhaeghe et al., Cell Reports 2023).

It is true that we aren’t currently modeling sensory signals explicitly. However, some of the optimal inputs we infer may be capturing upstream information which could englobe some sensory information. This is currently unclear, and would likely depend on how exactly the model is specified. We have added new discussion to emphasize that our dynamics should not be understood as just representing M1, but more general circuits whose state can be decoded from M1.

Reviewer #2 (Recommendations For The Authors):

Additionally, thank you for pointing out various typos in the manuscript, we have fixed those!

Reviewer 3:

Thank you very much for your review, which makes a lot of very insightful points, and raises several interesting questions. In summary, we very much agree with the limitations you pointed out. In particular, the choice of input cost is something we had previously discussed, but we had found it challenging to decide on what a reasonable cost for “complexity” could be. Following your comment, we have however added a first attempt at penalizing “temporal complexity”, which shows promising behavior. We have only included those additional analyses as supplementary figures, and we have included new discussion, which hopefully highlights what we meant by the different model components, and how the model behavior may change as we vary some of our choices. We hope this can be informative for future models that may use a similar approach. Below, we highlight the changes that we have made to address your comments.

The main limitation of the study is that it focuses exclusively on one specific constraint - magnitude - that could limit motor-cortex inputs. This isn't unreasonable, but other constraints are at least as likely, if less mathematically tractable. The basic results of this study will probably be robust with regard such issues - generally speaking, any constraint on what can be delivered during execution will favor the strategy of preparing - but this robustness cuts both ways. It isn't clear that the constraint used in the present study - minimizing upstream energy costs - is the one that really matters. Upstream areas are likely to be limited in a variety of ways, including the complexity of inputs they can deliver. Indeed, one generally assumes that there are things that motor cortex can do that upstream areas can't do, which is where the real limitations should come from. Yet in the interest of a tractable cost function, the authors have built a system where motor cortex actually doesn't do anything that couldn't be done equally well by its inputs. The system might actually be better off if motor cortex were removed. About the only thing that motor cortex appears to contribute is some amplification, which is 'good' from the standpoint of the cost function (inputs can be smaller) but hardly satisfying from a scientific standpoint.

The use of a term that punishes the squared magnitude of control signals has a long history, both because it creates mathematical tractability and because it (somewhat) maps onto the idea that one should minimize the energy expended by muscles and the possibility of damaging them with large inputs. One could make a case that those things apply to neural activity as well, and while that isn't unreasonable, it is far from clear whether this is actually true (and if it were, why punish the square if you are concerned about ATP expenditure?). Even if neural activity magnitude an important cost, any costs should pertain not just to inputs but to motor cortex activity itself. I don't think the authors really wish to propose that squared input magnitude is the key thing to be regularized. Instead, this is simply an easily imposed constraint that is tractable and acts as a stand-in for other forms of regularization / other types of constraints. Put differently, if one could write down the 'true' cost function, it might contain a term related to squared magnitude, but other regularizing terms would by very likely to dominate. Using only squared magnitude is a reasonable way to get started, but there are also ways in which it appears to be limiting the results (see below).

I would suggest that the study explore this topic a bit. Is it possible to use other forms of regularization? One appealing option is to constrain the complexity of inputs; a long-standing idea is that the role of motor cortex is to take relatively simple inputs and convert them to complex time-evolving inputs suitable for driving outputs. I realize that exploring this idea is not necessarily trivial. The right cost-function term is not clear (should it relate to low-dimensionality across conditions, or to smoothness across time?) and even if it were, it might not produce a convex cost function. Yet while exploring this possibility might be difficult, I think it is important for two reasons.

First, this study is an elegant exploration of how preparation emerges due to constraints on inputs, but at present that exploration focuses exclusively on one constraint. Second, at present there are a variety of aspects of the model responses that appear somewhat unrealistic. I suspect most of these flow from the fact that while the magnitude of inputs is constrained, their complexity is not (they can control every motor cortex neuron at both low and high frequencies). Because inputs are not complexity-constrained, preparatory activity appears overly complex and never 'settles' into the plateaus that one often sees in data. To be fair, even in data these plateaus are often imperfect, but they are still a very noticeable feature in the response of many neurons. Furthermore, the top PCs usually contain a nice plateau. Yet we never get to see this in the present study. In part this is because the authors never simulate the situation of an unpredictable delay (more on this below) but it also seems to be because preparatory inputs are themselves strongly time-varying. More realistic forms of regularization would likely remedy this.

That is a very good point, and it mirrors several concerns that we had in the past. While we did focus on the input norm for the sake of simplicity, and because it represents a very natural way to regularize our control solutions, we agree that a “complexity cost” may be better suited to models of brain circuits. We have addressed this in a supplementary investigation. We chose to focus on a cost that penalizes the temporal complexity of the inputs, as ||u(t+1) - u(t)||^2. Note that this required augmenting the state of the model, making the computations quite a bit slower; while it is doable if we only penalize the first temporal derivative, it would not scale well to higher orders.

Interestingly, we did find that the activity in that setting was somewhat more realistic (see new Supplementary Figure S8), with more sustained inputs and plateauing activity. While we have kept the original model for most of the investigations, the somewhat more realistic nature of the results under that setting suggests that further exploration of penalties of that sort could represent a promising avenue to improve the model.

We also found the idea of a cost that would ensure low-dimensionality of the inputs across conditions very interesting. However, it is challenging to investigate with iLQR as we perform the optimization separately for each condition; nevertheless, it could be investigated using a different optimizer.

At present, it is also not clear whether preparation always occurs even with no delay. Given only magnitude-based regularization, it wouldn't necessarily have to be. The authors should perform a subspace-based analysis like that in Figure 6, but for different delay durations. I think it is critical to explore whether the model, like monkeys, uses preparation even for zero-delay trials. At present it might or might not. If not, it may be because of the lack of more realistic constraints on inputs. One might then either need to include more realistic constraints to induce zero-delay preparation, or propose that the brain basically never uses a zero delay (it always delays the internal go cue after the preparatory inputs) and that this is a mechanism separate from that being modeled.

I agree with the authors that the present version of the model, where optimization knows the exact time of movement onset, produces a reasonably realistic timecourse of preparation when compared to data from self-paced movements. At the same time, most readers will want to see that the model can produce realistic looking preparatory activity when presented with an unpredictable delay. I realize this may be an optimization nightmare, but there are probably ways to trick the model into optimizing to move soon, but then forcing it to wait (which is actually what monkeys are probably doing). Doing so would allow the model to produce preparation under the circumstances where most studies have examined it. In some ways this is just window-dressing (showing people something in a format they are used to and can digest) but it is actually more than that, because it would show that the model can produce a reasonable plateau of sustained preparation. At present it isn't clear it can do this, for the reasons noted above. If it can't, regularizing complexity might help (and even if this can't be shown, it could be discussed).

In summary, I found this to be a very strong study overall, with a conceptually timely message that was well-explained and nicely documented by thorough simulations. I think it is critical to perform the test, noted above, of examining preparatory subspace activity across a range of delay durations (including zero) to see whether preparation endures as it does empirically. I think the issue of a more realistic cost function is also important, both in terms of the conceptual message and in terms of inducing the model to produce more realistic activity. Conceptually it matters because I don't think the central message should be 'preparation reduces upstream ATP usage by allowing motor cortex to be an amplifier'. I think the central message the authors wish to convey is that constraints on inputs make preparation a good strategy. Many of those constraints likely relate to the fact that upstream areas can't do things that motor cortex can do (else you wouldn't need a motor cortex) and it would be good if regularization reflected that assumption. Furthermore, additional forms of regularization would likely improve the realism of model responses, in ways that matter both aesthetically and conceptually. Yet while I think this is an important issue, it is also a deep and tricky one, and I think the authors need considerable leeway in how they address it. Many of the cost-function terms one might want to use may be intractable. The authors may have to do what makes sense given technical limitations. If some things can't be done technically, they may need to be addressed in words or via some other sort of non-optimization-based simulation.

Specific comments

As noted above, it would be good to show that preparatory subspace activity occurs similarly across delay durations. It actually might not, at present. For a zero ms delay, the simple magnitude-based regularization may be insufficient to induce preparation. If so, then the authors would either have to argue that a zero delay is actually never used internally (which is a reasonable argument) or show that other forms of regularization can induce zero-delay preparation.

Yes, that is a very interesting analysis to perform, which we had not considered before! When investigating this, we found that the zero-delay strategy does not rely on preparation in the same way as is seen in the monkeys. This seems to be a reflection of the fact that our “Go cue” corresponds to an “internal” go cue which would likely come after the true, “external go cue” – such that we would indeed never actually be in the zero delay setting. This is not something we had addressed (or really considered) before, although we had tried to ensure we referred to “delta prep” as the duration of the preparatory period but not necessarily the delay period. We have now included more discussion on this topic, as well as a new Supplementary Figure S10.

I agree with the authors that prior modeling work was limited by assuming the inputs to M1, which meant that prior work couldn't address the deep issue (tackled here) of why there should be any preparatory inputs at all. At the same time, the ability to hand-select inputs did provide some advantages. A strong assumption of prior work is that the inputs are 'simple', such that motor cortex must perform meaningful computations to convert them to outputs. This matters because if inputs can be anything, then they can just be the final outputs themselves, and motor cortex would have no job to do. Thus, prior work tried to assume the simplest inputs possible to motor cortex that could still explain the data. Most likely this went too far in the 'simple' direction, yet aspects of the simplicity were important for endowing responses with realistic properties. One such property is a large condition-invariant response just before movement onset. This is a very robust aspect of the data, and is explained by the assumption of a simple trigger signal that conveys information about when to move but is otherwise invariant to condition. Note that this is an implicit form of regularization, and one very different from that used in the present study: the input is allowed to be large, but constrained to be simple. Preparatory inputs are similarly constrained to be simple in the sense that they carry only information about which condition should be executed, but otherwise have little temporal structure. Arguably this produces slightly too simple preparatory-period responses, but the present study appears to go too far in the opposite direction. I would suggest that the authors do what they can to address these issue via simulations and/or discussion. I think it is fine if the conclusion is that there exist many constraints that tend to favor preparation, and that regularizing magnitude is just one easy way of demonstrating that. Ideally, other constraints would be explored. But even if they can't be, there should be some discussion of what is missing - preparatory plateaus, a realistic condition-invariant signal tied to movement onset - under the present modeling assumptions.

As described above, we have now included two additional figures. In the first one (S8, already discussed above), we used a temporal smoothness prior, and we indeed get slightly more realistic activity plateaus. In a second supplementary figure (S9), we have also considered using model predictive control (MPC) to optimize the inputs under an uncertain go cue arrival time. There, we found that removing the assumption that the delay period is known came with new challenges: in particular, it requires the specification of a “mental model” of when the Go cue will arrive. While it is reasonable to expect that monkeys will have a prior over the go time arrival cue that will be shaped by the design of the experiment, some assumptions must be made about the utility functions that should be used to weigh this prior. For instance, if we imagine that monkeys carry a model of the possible arrival time of the go cue that is updated online, they could nonetheless act differently based on this information, for instance by either preparing so as to be ready for the earliest go cue possible or alternatively to be ready for the average go cue. This will likely depend on the exact task design and reward/penalty structure. Here, we added simulations with those two cases (making simplifying assumptions to make the problem tractable/solvable using model predictive control), and found that the “earliest preparation” strategy gives rise to more realistic plateauing activity, while the model where planning is done for the “most likely go time” does not. We suspect that more realistic activity patterns could be obtained by e.g combining this framework with the temporal smoothness cost. However, the main point we wished to make with this new supplementary figure is that it is possible to model the task in a slightly more realistic way (although here it comes at the cost of additional model assumptions). We have now added more discussion related to those points. Note that we have kept our analyses on these new models to a minimum, as the main takeaway we wish to convey from them is that most components of the model could be modified/made more realistic. This would impact the qualitative behavior of the system and match to data but – in the examples we have so far considered – does not appear to modify the general strategy of networks relying on preparation.

On line 161, and in a few other places, the authors cite prior work as arguing for "autonomous internal dynamics in M1". I think it is worth being careful here because most of that work specifically stated that the dynamics are likely not internal to M1, and presumably involve inter-area loops and (at some latency) sensory feedback. The real claim of such work is that one can observe most of the key state variables in M1, such that there are periods of time where the dynamics are reasonably approximated as autonomous from a mathematical standpoint. This means that you can estimate the state from M1, and then there is some function that predicts the future state. This formal definition of autonomous shouldn't be conflated with an anatomical definition.

Yes, that is a good point, thank you for making it so clearly! Indeed, as previous work, we do not think of our “M1 dynamics” as being internal to M1, but they may instead include sensory feedback / inter-area loops, which we summarize into the connectivity, that we chose to have dynamics that qualitatively resemble data. We have now incorporated more discussion regarding what exactly the dynamics in our model represent.

Author response:

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

eLife assessment 

Dasgupta and colleagues make a valuable contribution to the understanding how the guidance factor Sema7a promotes connections between mechanosensory hair cells and afferent neurons of the zebrafish lateral line system. The authors provide solid evidence that loss of Sema7a function results in fewer contacts between hair cells and afferents through comprehensive quantitative analysis. Additional work is needed to distinguish the effects of different isoforms of Sema7a to determine whether there are specific roles of secreted and membrane bound forms. 

Public Reviews:

Reviewer #1 (Public Review):

Dasguta et al. have dissected the role of Sema7a in fine tuning of a sensory microcircuit in the posterior lateral line organ of zebrafish. They attempt to also outline the different roles of a secreted verses membrane-bound form of Sema7a in this process. Using genetic perturbations and axonal network analysis, the authors show that loss of both Sema7a isoforms causes abnormal axon terminal structure with more bare terminals and fewer loops in contact with presynaptic sensory hair cells. Further, they show that loss of Sema7a causes decreased number and size of both the pre- and post-synapse. Finally, they show that overexpression of the secreted form of Sema7a specifically can elicit axon terminal outgrowth to an ectopic Sema7a expressing cell. Together, the analysis of Sema7a loss of function and overexpression on axon arbor structure is fairly thorough and revealed a novel role for Sema7a in axon terminal structure. However, the connection between different isoforms of Sema7a and the axon arborization needs to be substantiated. Furthermore, the effect of loss of Sema7a on the presynaptic cell is not ruled out as a contributing factor to the synaptic and axon structure phenotypes. These issues weaken the claims made by the authors including the statement that they have identified dual roles for the GPI-anchored verses secreted forms of Sema7a on synapse formation and as a chemoattractant for axon arborization respectively. 

Reviewer #2 (Public Review):

In this work, Dasgupta et al. investigates the role of Sema7a in the formation of peripheral sensory circuit in the lateral line system of zebrafish. They show that Sema7a protein is present during neuromast maturation and localized, in part, to the base of hair cells (HCs). This would be consistent with pre-synaptic Sema7a mediating formation and/or stabilization of the synapse. They use sema7a loss-of-function strain to show that lateral line sensory terminals display abnormal arborization. They provide highly quantitative analysis of the lateral line terminal arborization to show that a number of specific topological parameters are affected in mutants. Next, they ectopically express a secreted form of Sema7a to show that lateral line terminals can be ectopically attracted to the source. Finally, they also demonstrate that the synaptic assembly is impaired in the sema7a mutant. Overall, the data are of high quality and properly controlled. The availability of Sema7a antibody is a big plus, as it allows to address the endogenous protein localization as well to show the signal absence in the sema7a mutant. The quantification of the arbor topology should be useful to people in the field who are looking at the lateral line as well as other axonal terminals. I think some results are overinterpreted though. The authors state: "Our findings demonstrate that Sema7A functions both as a juxtracrine and as a secreted cue to pattern neural circuitry during sensory organ development." However, they have not actually demonstrated which isoform functions in HCs (also see comments below). In addition, they have to be careful in interpreting their topology analysis, as they cannot separate individual axons. Thus, such analysis can generate artifacts. They can perform additional experiments to address these issues or adjust their interpretations. 

Reviewer #3 (Public Review):

The data reported here demonstrate that Sema7a defines the local behavior of growing axons in the developing zebrafish lateral line. The analysis is sophisticated and convincingly demonstrates effects on axon growth and synapse architecture. Collectively, the findings point to the idea that the diffusible form of sema7a may influence how axons grow within the neuromast and that the GPI-linked form of sema7a may subsequently impact how synapses form, though additional work is needed to strongly link each form to its' proposed effect on circuit assembly. 

The revised manuscript is significantly improved. The authors comprehensively and appropriately addressed most of the reviewers' concerns. In particular, they added evidence that hair cells express both Sema7A isoforms, showed that membrane bound Sema7A does not have long range effects on guidance, demonstrated how axons behave close to ectopic Sema7A, and analyzed other features of the hair cells that revealed no strong phenotypes. The authors also softened the language in many, but not all places. Overall, I am satisfied with the study as a whole. 

Reviewer #4 (Public Review):

This study provides direct evidence showing that Sema7a plays a role in the axon growth during the formation of peripheral sensory circuits in the lateral-line system of zebrafish. This is a valuable finding because the molecules for axon growth in hair-cell sensory systems are not well understood. The majority of the experimental evidence is convincing, and the analysis is rigorous. The evidence supporting Sema7a's juxtracrine vs. secreted role and involvement in synapse formation in hair cells is less conclusive. The study will be of interest to cell, molecular and developmental biologists, and sensory neuroscientists. 

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

In their revised manuscript, Dasgupta et al. have provided further experiments to address the role of Sema7a (sec and GPI-anchored) in regulating axon guidance in the lateral line system. Specifically, the inclusion of the heat shock controls and FM labeling to show hair cell mechanotransduction were crucial to interpretation of the results. However, there are still concerns about the specificity of the results. My primary concern is if the change in axon patterning is specifically due to loss of Sema7a in the mutant hair cells. These animals are morphologically very abnormal and, in the rebuttal, the authors state that hair cell number is reduced. This is not quantified in the manuscript and should be included. 

Thank you for this suggestion. We have included the data in the manuscript in lines 137-139, in Figure 2—figure supplement 1B, and in the source data for Figure 2 and Figure 2-figure supplements.

If there is not a function for Sema7a in hair cells themselves, why is the number reduced? 

The sema7a-/- homozygous mutants are not viable and they die by 6 dpf. The loss of Sema7A protein produce other developmental defects including brain edema and a curved body axis. We believe a slight but not significant decrease in hair cell number may arise from a minute developmental delay in the morphogenesis of the neuromast. We have accordingly quantified our data at three distinct developmental stages-at 2 dpf, 3 dpf, and 4 dpf-and have incorporated them in the revised manuscript.

Additionally, FM data should be quantified and presented in animals without a transgene in the same excitation/emission spectra for clearer interpretation of the staining.

We have quantified the intensities of labeling with FM 4-64 styryl dye from the control and the sema7a-/- mutant larvae and incorporated the data in lines 139-146, in Figure 2—figure supplement 1D, and in source data for Figure 2 and Figure 2-figure supplements. We Kept the transgenes to concurrently show the arborization phenotype, hair cell morphology, and the FM 4-64 incorporation between the genotypes. 

Rescue analysis using the myo6d promotor would allow the authors to ensure that the axon deficits can be rescued by putting Sema7a back into the sensory hair cells. Transient transgenesis could be useful for this approach and would not require the creation of a stable line. This could be done with both forms of Sema7a allowing the true assessment of whether or not the secreted and GPI-anchored form have disparate functions as claimed in lines 418424. 

Although we recognize the importance of the rescue of the sema7a-/- mutant phenotype with the sema7asec and the sema7aGPI transcripts, it is not possible for us to perform that experiment at the moment, for the first author will leave the lab next week.  However, he plans to continue work on this project as an independent investigator to dissect the individual roles of the transcript variants in specifying the pattern of sensory arborization, a project that includes generation of transcript-specific knockout animals and rescue experiments with stable transgenic fish lines. 

Other concerns:

(1) The timeline of the heat shock experiment is confusing to me and, therefore, it makes me question the specificity of those results. Based on the speed of axon outgrowth and the time necessary for transcription and translation after heat shock induction of the transgene, it is unclear to me how the axon growth defects could occur in the timeline provided. Imaging two hours after the start of the heat shock is very rapid and speaks to either an indirect effect of the transgenesis on the axon growth or a leaky promotor/induction paradigm. It is possible I am just misunderstanding the set up but, from what I could gather, the imaging is being done 2 hrs after the start of the heat shock. This should be clarified. 

The axons of the zebrafish posterior lateral line migrate relatively fast. The pioneering axons migrate at around 120 μm/hour (Sato et. al., 2010) and the follower axons migrate at almost 30-80 μm/hour (Sato et. al., 2010). The heat-shock promoter that we have utilized, hsp70l, is highly effective in inducing gene expression and subsequent protein formation within 30 to 60 mins. We believe an hour of heat shock and an hour of incubation post heat shock is sufficient to induce directed axon migration to a distance that spans from 27 μm to 140 μm. 

We strongly believe that the directed arborization of the sensory axons towards the Sema7Asec source is not due to an indirect effect of transgenesis or leaky promoter induction, as in all 18 of the injected but not heat-shocked control larvae we did not observe ectopic Sema7Asec expression, and no aberrant projection was formed from the sensory arbor network. We highlight this observation in lines 297-299 and in Figure 4E.

Sato et. al., 2010: Single-cell analysis of somatotopic map formation in the zebrafish lateral line system. Developmental Dynamics 239:2058–2065, 2010.

Similarly, it would help to clarify if t(0) in the figure is the onset of the heat shock or onset of imaging two hours after the heat shock is started. 

The t=0 hour in the Figure 4I denotes the onset of imaging two hours after the heat shock began. We have clarified this in the manuscript in lines 1155-1156.

(2) In the rebuttal, the line numbers cited do not match up with the appropriate text, I believe.

We have corrected this and updated the manuscript.

(3) Some of the supplemental figures are not mentioned in the text, or I could not find them. For example: Figure 1 supplement 2J. 

Thank you for pointing this. We have corrected the manuscript, and the new information is added in line 114.  

(4) Table 1 statistics: were these adjusted for multiple comparisons using a bonferroni correction or something similar? This is necessary for statistical significance to be meaningful. 

We did not adjust the p-values for multiple comparisons because the values correspond to only three or four statistical tests per experiment, strongly indicating the unlikelihood of erroneous significance due solely to multiple tests.

(5) Figure 1I and 1-S3 - The legend states a positive correlation between axonal signal and sema7A signal. Correlations are 0.5, 0.6, and 0.4 (2,3, 4dpf). This is not a convincing positive correlation. At best this is no to a very weak positive correlation. 

In lines 122-126 we mention that the basal association of the sensory arbors shows a positive correlation with Sema7A accumulation. We never emphasize on the strength of the correlation. However, a consistent positive correlation at three different developmental stages suggests that progressive Sema7A accumulation at the base of the hair cells may guide the sensory arbors to increasingly associate themselves with the hair cells.    

Reviewer #2 (Recommendations For The Authors):

I am a bit disappointed that the authors elected not to experimentally address the issue raised by all reviewers: whether the secreted or membrane bound isoform is active in hair cells. They rather decided to change their interpretation in the text. It is fine, given the eLife review structure. However, that would make the manuscript much stronger. Other issues were adequately addressed through textual changes as well. 

Although we recognize the importance of the rescue of the sema7a-/- mutant phenotype with the sema7asec and the sema7aGPI transcripts, it is not possible for us to perform that experiment at the moment, for the first author will leave the lab next week.  However, he plans to continue work on this project as an independent investigator to dissect the individual roles of the transcript variants in specifying the pattern of sensory arborization, a project that includes generation of transcript-specific knockout animals and rescue experiments with stable transgenic fish lines. 

Reviewer #3 (Recommendations For The Authors):

Overall, I am satisfied with the study as a whole and just have a few minor comments that remain to be addressed. 

(1) Although the authors say that they added appropriate no plasmid/heatshock-only and plasmid-only/no heatshock controls, these results need to be presented more clearly, as they are separated in the paper and only one was quantified (i.e. 100% of embryos showed no defect). Please just make it clear that no defects were observed in either control for either experiment (both secreted and membrane bound ectopic expression). 

We have clearly stated this information in lines 297-299 and 343-345.

(2) Please add a compass to Fig. 1A to indicate the orientation of the neuromast. It would also be helpful to add labels for developmental ages to all of the figures, rather than making the reader look it up in the legend. 

We have updated the Figure 1A and the corresponding figure legend in lines 882883 . We have denoted the larval age in the figure legends to keep the individual images uncluttered.  

(3) For the RT-PCR experiments in Figure 1, no negative control was included to show that supporting cell or neuronal genes are not detected in the purified hair cells and v.v. that neither isoform is detected in supporting cells or neurons. I ask only because there is a lot of immune-signal outside of the hair cells and I am curious whether that is secreted or might come from other cell types. For neurons and supporting cells, simply demonstrating absence of Sema7a overall would suffice. 

We have utilized the transgenic line Tg(myo6b:actb1-EGFP) that expresses the fluorophore GFP specifically in the hair cells of the neuromast. Unfortunately, we do not possess a transgenic line that reliably and specifically labels the support cells in the neuromast. Hence, in our sorting experiment the GFP-negative cells that are collected from the trunk segments of the larvae contain all the non-hair cells including epidermal cells, neuronal cells, and immune cells etc. Such a mixture of varied cellular identity may not serve as a reliable negative control. 

In Figure 7, we have plotted the normalized expression values of the sema7a gene in the neuromast. The plot clearly depicts that the source of Sema7A is the young and the mature hair cells, not the support cells. We further confirm this observation by

immunostaining where the Sema7A signal is highly restricted to the hair cells and not in any other cell in the neuromast (Figure 1E). Immunostaining further demonstrates that the lateral line sensory arbors also do not produce the Sema7A protein (Figure 1H; Video 1).

We agree with the reviewer that there are diverse immune cells, including macrophages in and around the neuromast. These macrophages are dynamic and possess highly ramified structure (Denans et. al., 2022). In all our Sema7A immunostainings, we never observed structures that resemble macrophages. Albeit we cannot confirm that Sema7A is not expressed in a distant immune cell, but we highly doubt that signal coming from immune cells is impacting hair cell innervation by the sensory arbors during homeostatic development.

Denans et. al., 2022: Nature Communications volume 13, Article number: 5356 (2022).

(4) In Figure 1, Supplement 4, I do not see the immunogen labeled in blue. 

We have corrected the figure legend. The immunogenic region of the Sema7A protein is now clearly denoted in the figure legend of Figure 1—figure supplement 4.

(5) In Figure 2, please add a control image as requested, as that enables direct comparison. There is ample room in the figure. 

We have updated the Figure 2 and made the suggested change.

(6) In Figure 2, Supplement 1, the FM4-64 data are not presented in a quantified fashion. Please report at least how many embryos showed reliable uptake and preferably how many hair cells per embryo showed reliable uptake. 

We have quantified the FM 4-64 intensities in control and sema7a-/- mutant larvae. The new data is added to the manuscript in lines 142-146, 577-579 , and in Figure 2—figure supplement 1D.

(7) In Figure 3, there seems to be a typo in the figure legend: "mutants in the same larvae" does not make sense to me. 

We have corrected the error. The modified statement is represented in lines 10671068.

(8) The text should refer more explicitly to the statistical tests reported in Table 1, i.e. as the results are presented. 

In lines 1105 and 1109, we clearly state the statistical tests that were performed.

(9) In Figure 6, Supplement 1, please show the raw data points not just the bar graphs

We have updated the Figure 6—figure supplement 1.

(10) Minor point: the authors state that they addressed the distance over which secreted Sema7A may act, but this was not evident to me in the text. Please make this finding clearer.

We have clarified this information in lines 310-311.

(11) Finally, the discussion contains a statement that is not supported by the data: "We have discovered dual modes of Sema7A function in vivo." They have discovered evidence that there are two isoforms, that loss of both disrupts connectivity, and that overexpression of only the secreted form can elicit growth from a distance. However, there is no direct evidence that the membrane-bound form is responsible for local effects. It is formally possible still that the phenotypes are a result of dual roles for the secreted form. It is clear that another manuscript is forthcoming that will expand on the role of the transmembrane form, but for this manuscript, the authors should make firm conclusions only about the data presented herein.

Thank you for this suggestion. We have modified the manuscript in lines 425-434.

Reviewer #4 (Recommendations For The Authors):

The authors have made significant changes to the manuscript based on the comments of the reviewers. It is now suitable for publication.

Author response:

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

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I have no more experiment to ask but the following errors should be corrected prior.

(1) L. 183-198: Figure 3 panels were erroneously referred in several places.

This has been corrected.

(2) L.182-183: description of active/total cell numbers in main text does not match numbers in Figure 3B

This has been corrected.

(3) L.185-187: Figure 3C indicates significant changes of rheobase only between DMI+6OHDA versus 6-OHDA group. Statistical comparison between sham and DMI+6-OHDA was not provided, which may change the interpretation of the data in Figure 3B, C: "...these findings suggest that the 6-OHDA induced lesion of midbrain dopaminergic neurons evoked the increased firing of DRN5-HT neurons" (L.185-187).

We thank the reviewer for highlighting this point. Indeed, a Kruskal-Wallis test comparing all three groups revealed a significantly lower rheobase in DMI + 6-OHDA mice compared to Sham while the 6-OHDA injected group was not affected. Therefore, the increased firing of DRN5-HT neurons recorded in 6-OHDA injected mice pretreated with DMI also critically involves the noradrenergic system. This is now included in the revised results section of the manuscript (lines 190-197).

(4) L. 188: The description of "While the excitability of DRN5-HT neurons was not affected in 6-OHDA mice..." does not match the clearly increased cellular excitability shown in Figure 3G-I.

This has been corrected and we are now referring more specifically to the rheobase, which is not affected in 6-OHDA mice.

(5) Mann-Whitney tests were inappropriately used for statistics in Figures 3-6: Multiple comparisons (>=3 groups) should be performed one-way ANOVA or the Kruskal-Wallis test for nonparametric data.

We thank the reviewer for the comment. We now applied the one-way ANOVA/KruskalWallis tests and the text has been modified accordingly.

(6) It seems that the data points in some panels of Figure 4C represented a cell, but others were averaged within a mouse (Figure 4D). This needs to be clarified or corrected.

None of the data in Figure 4 was averaged within a mouse. In the the type of chosen graph (aligned dot plot) the equal data are overlapped.

Reviewer #2 (Recommendations For The Authors):

The authors' revised manuscript has addressed most of my concerns. However, I'm not convinced by the authors' claim regarding Figure 5B. It would be great if the authors at least discuss in their manuscript why the DMI pretreatment group alone, not the 6OHDA group, significantly lowers the firing rate of DRN (DA) and increases the Erest of DRN (DA), compared to the sham-lesion group. These statistically significant data are not explained at all in the revised manuscript (This effect can be explained by the neuroprotection of NA-neurons from 6-OHDA toxicity?).

We thank the reviewer for this comment. Since using a one-way ANOVA or a KruskalWallis test for comparing the three groups (as suggested by reviewer 1), the changes previously shown in Figure 5B are not significant.

Author response:

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

eLife assessment

This manuscript represents a cleanly designed experiment for assessing biological motion processing in children (mean age = 9) with and without ADHD. The group differences concerning accuracy in global and local motion processing abilities are solid, but the analyses suggesting dissociable relationships between global and local processing and social skills, age, and IQ are inconclusive. The results are useful in terms of understanding ADHD and the ontogenesis of different components of the processing of biological motion.

We thank the editors and reviewers for their valuable feedback and constructive comments. We have carefully considered each point raised by the reviewers and made the necessary revisions to the manuscript. Regarding the relationships between global and local BM processing, the accumulated evidence from previous studies has converged on the dissociation of the two BM components, e.g., while global BM processing is susceptible to learning and practice, local BM processing does not show a learning trend (Chang and Troje, 2009; Grossman et al., 2004), and the brain activations in response to local and global BM cues are different (Chang et al., 2018; Duarte et al., 2022). Nevertheless, we concurred with reviewers that the evidence for such dissociation from the current study by itself is not strong enough. Therefore, we have toned down on this point and no longer claimed the dissociation (including the title). Based on the current results, we focused our discussion on the different aspects of BM processing in children with and without ADHD.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The paper presents a nice study investigating the impairments of biological motion perception in individuals with ADHD in comparison with neurotypical controls. Motivated by the idea that there is a relationship between biological motion perception and social capabilities, the authors investigated the impairments of local and global (holistic) biological motion perception, the diagnosis status, and several additional behavioral variables that are affected in ADHS (IQ, social responsiveness, and attention / impulsivity). As well local as global biological motion perception is impaired in ADHD individuals. In addition, the study demonstrates a significant correlation between local biological motion perception skills and the social responsiveness score in the ADHD group, but not in controls. A path analysis in the ADHD group suggests that general performance in biological motion perception is influenced mainly by global biological motion perception performance and attentional and perceptual reasoning skills.

Strengths:

It is true that there exists not much work on biological motion perception and ADHD. Therefore, the presented study contributes an interesting new result to the biological motion literature, and adds potentially also new behavioral markers for this clinical group. The design of the study is straightforward and technically sound, and the drawn conclusions are supported by the presented results.

Thanks for this positive assessment of our work.

Weaknesses:

Some of the claims about the relationship between genetic factors and ADHD and the components of biological motion processing have to remain speculative at this point because genetic influences were not explicitly tested in this paper. Specifically, the hypothesis that the perception of human social interaction is critically based on a local mechanism for the detection of asymmetry in foot trajectories of walkers (this is what 'BL-local' really measures), or on the detection of live agents in cluttered scenes seems not very plausible.

Thanks for these comments. We agree that the relationship between genetic factors and BM perception remains to be further examined, as we did not test the genetic influences in this study. We have deleted relavant discussion about genetics. Based on our results, we discuss the possible mechanisms behind the relationship between local BM processing and social interaction in the revised manuscript as follows:

“As mentioned above, we found a significant negative correlation between the SRS total score and the accuracy of local BM processing, specifically in the ADHD group. This could be due to decreased visual input related to atypical local BM processing, which further impairs global BM processing. According to the two-process theory of biological motion processing61, local BM cues guide visual attention towards BM stimuli55,62. Consequently, the visual input of BM stimuli increases, facilitating the development of the ability to process global BM cues through learning21,63. The latter is a prerequisite for attributing intentions to others and facilitating social interactions with other individuals20,64,65. Thus, atypical local BM processing may contribute to impaired social interaction through altered visual inputs. Further empirical studies are required to confirm these hypotheses.” (lines 417 - 428)

Based on my last comments, now the discussion has been changed in a way that tries to justify the speculative claims by citing a lot of other speculative papers, which does not really address the problem. For example, the fact that chicks walk towards biological motion stimuli is interesting. To derive that this verifies a fundamental mechanism in human biological motion processing is extremely questionable, given that birds do not even have a cortex. Taking the argumentation of the authors serious, one would have to assume that the 'Local BM' mechanism is probably located in the mesencephalon in humans, and then would have to interact in some way with social perception differences of ADHD children. To me all this seems to make very strong (over-)claims. I suggest providing a much more modest interpretation of the interesting experimental result, based on what has been really experimentally shown by the authors and closely related other data, rather than providing lots of far-reaching speculations.

In the same direction, in my view, go claims like 'local BM is an intrinsic trait' (L. 448) , which is not only imprecise (maybe better 'mechanisms of processing of local BM cues') but also rather questionable. Likely, this' local processing of BM' is a lower level mechanisms, located probably in early and mid-levels of the visual cortex, with a possible influence of lower structures. It seems not really plausible that this is related to a classical trait variables in the sense of psychology, like personality, as seems to be suggested here. Also here I suggest a much more moderate and less speculative interpretation of the results.

We thank the reviewer for pointing out these issues. According to these comments, we have carefully revised the discussion to avoid strong (over-) claims. We have deleted the example of chicks, but substituted with more empirical studies to explain our results. We agree that the Local BM mechanism is probably located in subcortical regions in humans, which were reported by some MRI studies (Chang et al., 2018; Hirai and Senju, 2020; Loula et al., 2005). We have added some evidence that atypical local BM processing may decrease visual inputs related to social information as follows:

“According to the two-process theory of biological motion processing61, local BM cues guide visual attention towards BM stimuli55,62. Consequently, the visual input of BM stimuli increases, facilitating the development of the ability to process global BM cues through learning21,63. The latter is a prerequisite for attributing intentions to others and facilitating social interactions with other individuals20,64,65. Thus, atypical local BM processing may contribute to impaired social interaction through altered visual inputs.” (lines 421 - 427)

We have also deleted the clarims of 'local BM is an intrinsic trait' (originally L. 448) and related discussion as it was not conclusive based on the current study.

Reviewer #2 (Public Review):

Summary:

Tian et al. aimed to assess differences in biological motion (BM) perception between children with and without ADHD, as well as relationships to indices of social functioning and possible predictors of BM perception (including demographics, reasoning ability and inattention). In their study, children with ADHD showed poorer performance relative to typically developing children in three tasks measuring local, global, and general BM perception. The authors further observed that across the whole sample, performance in all three BM tasks was negatively correlated with scores on the social responsiveness scale (SRS), whereas within groups a significant relationship to SRS scores was only observed in the ADHD group and for the local BM task. Local and global BM perception showed a dissociation in that global BM processing was predicted by age, while local BM perception was not. Finally, general (local & global combined) BM processing was predicted by age and global BM processing, while reasoning ability mediated the effect of inattention on BM processing.

Strengths:

Overall, the manuscript is presented in a clear fashion and methods and materials are presented with sufficient detail so the study could be reproduced by independent researchers. The study uses an innovative, albeit not novel, paradigm to investigate two independent processes underlying BM perception. The results are novel and have the potential to have wide-reaching impact on multiple fields.

We appreciate the reviewer’s positive feedback very much.

Weaknesses:

The manuscript has greatly improved in clarity and methodological considerations in response to the review. There are only a few minor points which deserve the authors' attention:

When outlining the moviation for the current study, results from studies in ADHD and ASD are used too interchangeably. The authors use a lack of evidence for contributing (psychological/developmental) factors on BM processing in ASD to motivate the present study and refer to evidence for differences between typical and non-typical BM processing using studies in both ASD and ADHD. While there are certainly overlapping features between the two conditions/neurotypes, they are not to be considered identical and may have distinct etiologies, therefore the distinction between the two should be made clearer.

We thank the reviewer for pointing out this issue. We have removed some unnecessary citations about ASD and referred to studies about social cognition in ADHD to elaborate the motivation of this study:

“Further exploration of a diverse range of social cognitions (e.g., biological motion perception) can provide a fresh perspective on the impaired social function observed in ADHD. Moreover, recent studies have indicated that the social cognition in ADHD may vary depending on different factors at the cognitive, pathological, or developmental levels, such as general cognitive impairment5, symptoms severity8, or age5. Nevertheless, understanding how these factors relate to social cognitive dysfunction of in ADHD is still in its infancy. Bridging this gap is crucial as it can help depict the developmental trajectory of social cognition and identify effective interventions for impaired social interaction in individuals with ADHD.” (lines 53 - 62)

In the first/main analysis, is unclear to me why in the revised manuscript the authors changed the statistical method from ANOVA/ANCOVA to independent samples t-tests (unless the latter were only used for post-hoc comparisons, then this needs to be stated). Furthermore, although p-values look robust, for this analysis too it should be indicated whether and how multiple comparison problems were accounted for.

Thanks for the reviewer’s comments. According to the suggestions from reviewer #3, it may be inapposite to regard gender as a covariate in ANOVA, which may violate the assumptions of ANCOVA. To ensure that gender does not influence the results, firstly, we separated boys and girls on the plots with different coloured individual data points, and there are no signs of a gender effect in their TD group. Secondly, we use t-tests to examine the difference between TD and ADHD groups. Finally, we conducted a subsampling analysis with balanced data, and the results remained consistent.

In part 1 of the results, we aimed to compare the task accuracies between the TD and ADHD groups in three independent tasks, which assess the participants’ abilities to process three types of BM cues. We assumed that individuals with ADHD show poorer performance in three tasks compared to TD individuals. With regard to that, we consider that multiple comparisons may not be necessary.

Reviewer #3 (Public Review):

Strengths:

The authors present differences between ADHD and TD children in biological motion processing, and this question has not received as much attention as equivalent processing capabilities in autism. They use a task that appears well controlled. They raise some interesting mechanistic possibilities for differences in local and global motion processing, which are distinctions worth exploring. The group differences will therefore be of interest to those studying ADHD, as well as other developmental conditions, and those examining biological motion processing mechanisms in general.

We appreciate the reviewer’s positive assessment of this work.

Weaknesses:

The data are not strong enough to support claims about differences between global and lobal processing wrt social communication skills and age. The mechanistic possibilities for why these abilities may dissociate in such a way are interesting, but the crucial tests of differences between correlations do not present a clear picture. Further empirical work would be needed to test the authors' claims. Specifics:

The authors state frequently that it was the local BM task that related to social communication skills (SRS) and not the global tasks. However, the results section shows a correlation between SRS and all three tasks. The only difference is that when looking specifically within the ADHD group, the correlation is only significant for the local task. The supplementary materials demonstrate that tests of differences between correlations present an incomplete picture. Currently they have small samples for correlations, so this is unsurprising.

Thanks for this comment. We agree with the reviewer that the relationship between local and global processing with social communication and age needs more expirical work. Based on our results, there are only possible dissociable roles of local and global BM processing. The accumulated evidence from previous studies has converged on this dissociation, e.g., whild global BM processing is susceptible to learning and practice, local BM processing does not show a learning trend (Chang and Troje, 2009; Grossman et al., 2004), and the brain activations in response to local and global BM cues are different (Chang et al., 2018; Duarte et al., 2022). We concurred with reviewers that the evidence for such dissociation from the current study by itself is not strong enough. Therefore, we have toned down on this point and no longer emphasized the dissociation. Based on the current results, we focused our discussion on the different aspects of BM processing in children with and without ADHD. Future studies with larger sample sizes are needed to confirm this disociable relationship.

Theoretical assumptions. The authors make some statements about local vs global biological motion processing that should still be made more tentatively. They assume that local processing is specifically genetically whereas global processing is a product of experience. These data in newborn chicks are controversial and confounded - I cannot remember the specifics but I think there an upper vs lower visual field complexity difference here.

We appreciate the reviewer’s suggestion. We agree that the relationship between genetic factors and BM perception remains to be further examined as we didn’t perform any genetic analysis in the current study. Some speculative papers have been removed, so do the statement about newborn chicks given the controversial and confounded results. We have toned down our claims and povided a moderate interpretation of the results:

“Sensitivity to local BM cues emerges early in life54,55 and involves rapid processing in the subcortical regions16,56-58. As a basic pre-attentive feature23, local BM cues can guide visual attention spontaneously59,60. In contrary, the ability to process global BM cues is related to slow cortical BM processing and is influenced by many factors such as attention25,26 and visual experience21,51. As mentioned above, we found a significant negative correlation between the SRS total score and the accuracy of local BM processing, specifically in the ADHD group. This could be due to decreased visual input related to atypical local BM processing, which further impairs global BM processing. According to the two-process theory of biological motion processing61, local BM cues guide visual attention towards BM stimuli55,62. Consequently, the visual input of BM stimuli increases, facilitating the development of the ability to process global BM cues through learning21,63. The latter is a prerequisite for attributing intentions to others and facilitating social interactions with other individuals20,64,65. Thus, atypical local BM processing may contribute to impaired social interaction through altered visual inputs.” (lines 413 - 427)

“Few developmental studies have been conducted on local BM processing. The ability to process local BM cues remained stable and did not exhibit a learning trend21,25. A reasonable interpretation may be that local BM processing is a low-level mechanism, probably performed by the primary visual cortex and subcortical regions such as the superior colliculus, pulvinar, and ventral lateral nucleus14,56,61.” (lines 441- 446)

Readability. The manuscript needs very careful proofreading and correction for grammar. There are grammatical errors throughout.

Thank the reviewer for this feedback. We have performed thorough proofreading and corrected grammatical errors throughout the manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I thank the authors for their revisions that address several of the minor points that I raised in my last review. A number of requests are still not sufficiently answered:

L. 290 ff.: These model 'BM-local = age + gender etc ' is a pretty sloppy notation. I think what is meant that a GLM was used that uses the predictors genderetc. time appropriate beta_i values. This formulas should be corrected or one just says that a GLM was run with the predictors gender

The same criticism applies to these other models that follow.

This was corrected.

However, the corrected text remains sloppy: example: 'BM-locaL = ...' What exacty is 'BM-Local' the accuracy? etc. Here a precise notation shoudl be given that clearly names which variables are used here as predictors and target variables.

We appreciate the reviewer’s suggestion. We clarified which variables are used in our model and gived them precise notations:

“Three linear models were built to investigate the contributing factors: (a) ACClocal = β0 + β1 * age + β2 * gender + β3 * FIQ + β4 * QbInattention, (b) ACCglobal = β0 + β1 * age + β2 * gender + β3 * FIQ + β4 * QbInattention, and (c) ACCgeneral = β0 + β1 * age + β2 * gender + β3 * FIQ + β4 * QbInattention + β5 * ACClocal + β6 * ACCglobal. ACClocal, ACCglobal and ACCgeneral refer to the response accuracies of the three tasks in the ADHD group, and QbInattention is the standardised score for sustained attention function.” (lines 337 - 343)

All these models assume linearity of the combination of the predictors. was this assumption verified?

We referred to the previous study of BM perception in children. They found main predictor variables, including IQ (Rutherford et al., 2012; Jones et al., 2011) and age (Annaz et al., 2010; van et al., 2016), have a linear relation with the ability of BM processing.

This answer is insufficient and not convincing. Because a variable Y depends linearly on predictor A and B in some other study, this does not imply that is is also linear in predictor C, or does not show interactions with such predictors in the present study.

What is needed here is the testing of models with interaction terms and verifying that such models are not better predictors. If authors do not want to do this, they need at least to clearly point out that they made the strong assumption of linearity of their model, which might be wrong and thus be a substantial limitation of their analysis.

Thanks for the suggestion. We tried to compare each possible mode with and without relative interactions. The results showed that the change of Coefficient of Determination (R-squared, R2) between the two models was not statistically significant.

L. 296ff.: For model (b) it looks like general BM performance is strongly driven by the predictor global BM performance in the ADHD group. Does the same observation also apply to the controls?

The same phenomenon was not observed in TD children. We have briefly discussed this point in the Discussion section of the revised manuscript (lines 449 - 459).

Was such a path analysis also done for the TD subjects or not? If yes, was then also predicted that the variable BM-Global largely and directedly influences the variable BM-General? (The answer refers to the general discussion section, where no such analysis is presented, as far as I understand.)

Thank you for your comment. We also conduct a path analysis similar to that in the ADHD group. There is no statistically significant mediator effect in the TD group. Please see Figure S3 for complete statistics.

Reviewer #2 (Recommendations For The Authors):

(1) Please add public access to the data repository so data availability can be assessed.

The data analyzed during the study is available at https://osf.io/37p5s/.

(2) Lines 119-115: The differences observed in ADHD participants in the studies referenced here were relative to what group? The last sentence here also refers to two groups, and it is difficult to gather which specific groups are meant, also because the two references relate to both ADHD and ASD samples. Please clarify.

The suggestion is well taken. We have clarified the expressions accordingly:

“Specifically, compared with the typically developing (TD) group, children with ADHD showed reduced activity of motion-sensitive components (N200) while watching biological and scrambled motions, although no behavioural differences were observed. Another study found that children with ADHD performed worse in BM detection with moderate noise ratios than the TD group32.” (lines 100 - 105)

(3) Line 116: I'm not sure what is meant by 'despite initial indications' - please briefly specify/summarise here why the investigation into BM processing in ADHD is warranted.

Thank the reviewer for pointing out this issue. We rephrase this part and briefly specify “why the investigation into BM processing in ADHD is warranted”:

“Despite initial findings about atypical BM perception in ADHD, previous studies on ADHD treated BM perception as a single entity, which may have led to misleading or inconsistent findings28. Hence, it is essential to deconstruct BM processing into multiple components and motion features.” (lines 108 -111)

(4) Lines 290-293: Please complete the sentence.

Thank the reviewer for pointing out this issue. Th sentence has been completed:

“For Task 2 and 3, where children were asked to detect the presence or discriminate the facing direction of the target walker, TD group have higher accuracies than the ADHD group (Task 2 - TD: 0.70 ± 0.12, ADHD: 0.59 ± 0.12, t73 = 3.677, p < 0.001, Cohen's d = 0.861; Task 3 - TD: 0.79 ± 0.12, ADHD: 0.63 ± 0.17, t73 = 4.702, p < 0.001, Cohen's d = 1.100).” (lines 284 - 288)

Reviewer #3 (Recommendations For The Authors):

(1) Conclusions concerning differences between the local and global tasks wrt SRS and age (see above). I believe the authors need to reword throughout to reflect that the tests of differences between these crucial correlations did not present a clear picture.

We have reworded throughout the paper to reflect the inconclusiveness with regard to the relationship between local and global processing with social communication based on this study only. Future studies with larger sample sizes are needed to confirm this conclusion. The mechanism for this dissociable relationship should be validated by more psychologial tests in the future studies.

(2) I would again tone down the discussion of genetic specification of local processing, given it is highly controversial.

We thank the reviewer for pointing out the issue. We agree the point about the genetic specification of local processing remains controversial. The interpretation of results about local BM processing has been rephrased. Please refer to our response to the point #2 mentioned.

(3) The manuscript needs very careful proofreading and grammatical correction throughout.

Thanks for the suggestion to check the grammar. We have carefully proofread the manuscript to correct grammatical errors

Author response:

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

eLife assessment

Following synaptic vesicle fusion events at release sites, vesicle remnants will need to be cleared in order to allow new rounds of vesicle docking and fusion. This fundamental study of Mahapatra and Takahashi examines the role of release site clearance in synaptic transmission during repetitive activity in two types of central synapses, the giant calyx of Held and hippocampal CA1 synapses. The study uses pharmacological approaches to interfere with release site clearance by blocking membrane retrieval (endocytosis). They compare the effects on short-term plasticity with those obtained by pharmacologically inhibiting scaffold protein activity. The data presented make a compelling case for fast endocytosis as necessary for rapid site clearance and vesicle recruitment to active zones. The data reveal an unexpected, fast role for local site clearance in counteracting synaptic depression.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The study examines the role of release site clearance in synaptic transmission during repetitive activity under physiological conditions in two types of central synapses, calyx of Held and hippocampal CA1 synapses. After acute block of endocytosis by pharmacology, deeper synaptic depression or less facilitation was observed in two types of synapses. Acute block of CDC42 and actin polymerization, which possibly inhibits the activity of Intersectin, affected synaptic depression at the calyx synapse, but not at CA1 synapses. The data suggest an unexpected, fast role of the site clearance in counteracting synaptic depression.

Strengths:

The study uses acute block of the molecular targets with pharmacology together with precise electrophysiology. The experimental results are clear cut and convincing. The study also examines the physiological roles of the site clearance using action potential-evoked transmission at physiological Ca and physiological temperature at mature animals. This condition has not been examined.

Weaknesses:

Pharmacology may have some off-target effects, though acute manipulation should be appreciated and the authors have tried several reagents to verify the overall conclusions.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Mahapatra and Takahashi report on the physiological consequences of pharmacologically blocking either clathrin and dynamin function during compensatory endocytosis or of the cortical actin scaffold both in the calyx of Held synapse and hippocampal boutons in acute slice preparations

Strengths:

Although many aspects of these pharmacological interventions have been studied in detail during the past decades, this is a nice comprehensive and comparative study, which reveals some interesting differences between a fast synapse (Calyx of Held) tuned to reliably transmit at several 100 Hz and a more slow hippocampal CA1 synapse. In particular the authors find that acute disturbance of the synaptic actin network leads to a marked frequency-dependent enhancement of synaptic depression in the Calyx, but not in the hippocampal synapse This striking difference between both preparations is the most interesting and novel finding.

Weaknesses:

Unfortunately, however, these findings concerning the different consequences of actin depolymerization are not sufficiently discussed in comparison to the literature. My only criticism concerns the interpretation of the ML 141 and Lat B data. With respect to the Calyx data, I am missing a detailed discussion of the effects observed here in light of the different RRP subpools SRP and FRP. This is very important since Lee at al. (2012, PNAS 109 (13) E765-E774) showed earlier that disruption of actin inhibits the rapid transition of SRP SVs to the FRP at the AZ. The whole literature on this important concept is missing. Likewise, the role of actin for the replacement pool at a cerebellar synapse (Miki et al., 2016) is only mentioned in half a sentence. There is quite some evidence that actin is important both at the AZ (SRP to FRP transition, activation of replacement pool) and at the peri-active zone for compensatory endocytosis and release site clearance. Both possible underlying mechanisms (SRP to FRP transition or release site clearance) should be better dissected.

We dissected the latrunculin effect further by referring to the related literature within the scope of this study in the revised Discussion section (last paragraph).

Reviewer #3 (Public Review):

The manuscript by Mahapatra and Takahashi addresses the role of presynaptic release site clearance during sustained synaptic activity. The authors characterize the effects of pharmacologically interfering with SV endocytosis (pre-incubation with Dynasore or Pitstop-2) on synaptic short-term plasticity (STP) at two different CNS synapses (calyx of Held synapses and hippocampal SC to CA1 synapses) using patch-clamp recordings in acute slices under experimental conditions designed to closely mimic a physiological situation (37{degree sign}C and 1.3 mM external [Ca2+]). Endocytosis blocker-induced changes in STP and in the recovery from short-term depression (STD) are compared to those seen after pharmacologically inhibiting actin filament assembly (pre-incubation with Latrunculin-B or the selective Cdc42 GTPase inhibitor ML-141). Presynaptic capacitance (Cm) recordings in calyx terminals were used to establish the effects of the pharmacological maneuvers on SV endocytosis.

Latrunculin-B and ML-141 neither affect SV endocytosis (assayed by Cm recordings) nor EPSC recovery following conditioning trains, but strongly enhances STD at calyx synapses. No changes in STP were observed at Latrunculin-B- or ML-141-treated SC to CA1 synapses.

Dynasore and Pitstop-2 slow down endocytosis, limit the total amount of exocytosis in response to long stimuli, enhance STD in response to 100 Hz stimulation, but profoundly accelerate EPSC recovery following conditioning 100 Hz trains at calyx synapses. At SC to CA1 synapses, Dynasore and Pitstop-2 reduce the extend of facilitation and lower relative steady-state EPSCs suggesting a change in the facilitation-depression balance in favor of the latter.

The authors use state-of-the art techniques and their data, which is clearly presented, leads to authors to conclude that endocytosis is universally important for clearance of release sites while the importance of scaffold protein-mediated site clearance is limited to 'fast synapses'.

Unfortunately, and perhaps not completely unexpected in view of the pharmacological tools chosen, there are several observations which remain difficult to understand:

(1) Blocking site clearance affects release sites that have previously been used, i.e. sites at which SV fusion has occurred and which therefore need to be cleared. Calyces use at most 20% of all release sites during a single AP, likely fewer at 1.3 mM external [Ca2+]. Even if all those 20% of release sites become completely unavailable due to a block of release site clearance, the 2nd EPSC in a train should not be reduced by >20% because ~80% of the sites cannot be affected. However, ~50% EPSC reduction was observed (Fig. 2B1, lower right panel) raising the possibility that Dynasore does more than specifically interfering with SVs endocytosis (and possibly Pitstop as well). Non-specific effects are also suggested by the observed two-fold increase in initial EPSC size in SC to CA1 synapses after Dynasore pre-incubation.

This study compares different experimental conditions to conclude the physiological role of endocytosis on rapid neurotransmission at the large calyceal synapse in mice. A related study at the Drosophila neuromuscular junction (Kawasaki et al., Nat. Neuroscience 2000) reported similar findings in comparable experimental settings (physiological conditions and acute block of endocytosis).

(2) More severe depression was observed at calyx synapses after blocking endocytosis which the authors attribute to a presynaptic mechanism affecting pool replenishment. When probing EPSC recovery after conditioning 100 Hz trains, a speed up was observed mediated by an "unknown mechanism" which is "masked in 2 mM [Ca2+]". These two observations, deeper synaptic depression during 100 Hz but faster recovery from depression following 100 Hz, are difficult to align and no attempt was made to find an explanation.

By varying temperature (PT vs RT), calcium concentration (1.3 mM vs 2.0 mM), and stimulation frequency (10, 100, and 200 Hz; some data are not shown), the effect of endocytosis block on EPSC STD and recovery from STD kinetics at the post-hearing calyx were compared in these settings: (PT, 1.3 mM [Ca2+]), (PT, 2.0 mM Ca2+), and (RT, 2.0 mM [Ca2+]), to dissect their respective role.

(3) To reconcile previous data reporting a block of Ca2+-dependent recovery (CDR) by Dynasore or Latrunculin (measured at 2 mM external [Ca2+]) with the data presented here (using 1.3 mM external [Ca2+]) reporting no effect or a speed up of recovery from depression, the authors postulate that "CDR may operate only when excessive Ca2+ enters during massive presynaptic activation" (page 10 line 244). While that is possible, such explanation ignores plenty of calyx studies demonstrating fiber stimulation-induced CDR and elucidating molecular pathways mediating fiber stimulation-induced CDR, and it also completely dismisses the strong change in recovery time course after 10 Hz conditioning (single exponential) as compared to 100 Hz conditioning (double exponential with a pronounced fast component).

Strong presynaptic stimuli such as those illustrated in Figs. 1B,C induce massive exocytosis. The illustrated Cm increase of 2 to 2.5 pF represents fusion of 25,000 to 30,000 SVs (assuming a single SV capacitance of 80 aF) corresponding to a 12 to 15% increase in whole terminal membrane surface (assuming a mean terminal capacitance of ~16 pF). Capacitance measurements can only be considered reliable in the absence of marked changes in series and membrane conductance. Documentation of the corresponding conductance traces is therefore advisable for such massive Cm jumps and merely mentioning that the first 450 ms after stimulation were skipped during analysis or referring to previous publications showing conductance traces is insufficient.

All bar graphs in Figures 1 through 6 and Figures S3 through S6 compare three or even four (Fig. 5C) conditions, i.e. one control and at least two treatment data sets. It appears as if repeated t-tests were used to run multiple two-group comparisons (i.e. using the same control data twice for two different comparisons). Either a proper multiple comparison test should be used or a Bonferroni correction or similar multiple-comparison correction needs to be applied.

We updated the statistical analysis of all data using one-way ANOVA and t-test with BonferroniHolm method of p level correction and rectified one analysis in Fig 1 and 3, all major conclusions are unchanged.

Finally, the terminology of contrasting "fast-signaling" (calyx synapses) and "slow-plastic" (SC synapses) synapses seems to imply that calyx synapses lack plasticity, as does the wording "conventional bouton-type synapses involved in synaptic plasticity" (page 11, line 251). I assume, the authors primarily refer to the maximum frequencies these two synapse types typically transmit (fast-signaling vs slow-signaling)?

Properties of these two synapses described explicitly in updated text and they are renamed as fast and slow synapes.

Recommendations for the authors:

Reviewer #3 (Recommendations For The Authors):

'SV replenishment' and 'site clearance' should not be used synonymously as it seems to be done sometimes here.

In this revision, we described them more explicitly.

The data presented in Fig. S6 are detached from the rest of the manuscript, not relevant and should be removed. page 4 line 95 "... to ensure sufficient Ca2+ currents to induce exo-endocytosis." ICa is large enough to induce exocytosis also at 1.3 mM Ca2+. Please clarify.

We updated the relevant section.

page 5, line 108 "... this slow endocytosis showed a strongly prolonged time course without accompanied by the change of Cm or presynaptic Ca2+ currents" Please fix.

Fixed.

page 5, line 121 "Thus, at calyces of Held, bath-application of Dynasore or Pitstop-2 can block both fast and slow endocytosis without perturbing presynaptic intracellular milieu." Bath-application never perturbs the intracellular milieu. Please clarify.

Rephrased.

page 6 line 128 "... physiological aCSF" is a misnomer (= physiological artificial CSF). Please fix.

In the introduction section, it is clearly described.

page 11, line 252 "... from hippocampal SC-CA1 pyramidal neurons" There are no "SC-CA1 pyramidal neurons". Please fix.

Fixed.

page 12, line 285 "In acute slices optimized to physiological conditions" The conditions are optimized, not the slices. Please fix.

Fixed.

page 14, line 323 same as above

Fixed.

page 14, line 330 LTP at SC-CA1 synapses is postsynaptic. Please clarify.

Rephrased

page 16, line 381 "had a series resistance of 3-4 MOhm" versus

page 17, line 408 "The patch pipettes had a series resistance of 5-15 MOhm (less than 10 MOhm in most cells)" 3-4 is perhaps pipette resistance while 5-15 is perhaps series resistance? Please clarify.

Fixed.

page 17, line 398 "Cm traces were averaged at every 10 ms (for 10 Hz train stimulation) or 20 ms (for 5 ms single or 1 Hz train stimulation)." Do you mean to say that Cm traces were smoothed with a moving average using a window size of 10 or 20 ms duration? Please clarify.

Rephrased to clarify better.

page 18, "All values are given as mean {plus minus} SEM and significance of difference was evaluated by Student's unpaired t-test, unless otherwise noted." Please check. You cannot simply use repeated t-tests for multiple comparisons. Either a proper multiple comparison test should be used or a Bonferroni correction or similar multiple-comparison correction needs to be applied.

All statistical analysis are updated using one-way ANOVA and t-test, with Bonferroni-Holm method of p level correction and one analysis is rectified in Fig 1 and 3, with no change in major conclusions.

Author response:

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

Public Reviews:

Reviewer #1:

Summary:

The authors aim to test the sensory recruitment theory of visual memory, which assumes that visual sensory areas are recruited for working memory, and that these sensory areas represent visual memories in a similar fashion to how perceptual inputs are represented. To test the overlap between working memory (WM) and perception, the authors use coarse stimulus (aperture) biases that are known to account for (some) orientation decoding in the visual cortex (i.e., stimulus energy is higher for parts of an image where a grating orientation is perpendicular to an aperture edge, and stimulus energy drives decoding). Specifically, the authors show gratings (with a given "carrier" orientation) behind two different apertures: one is a radial modulator (with maximal energy aligned with the carrier orientation) and the other an angular modulator (with maximal energy orthogonal to the carrier orientation). When the subject detects contrast changes in these stimuli (the perceptual task), orientation decoding only works when training and testing within each modulator, but not across modulators, showing the impact of stimulus energy on decoding performance. Instead, when subjects remember the orientation over a 12s delay, orientation decoding works irrespective of the modulator used. The authors conclude that representations during WM are therefore not "sensory-like", given that they are immune to aperture biases. This invalidates the sensory recruitment hypothesis, or at least the part assuming that when sensory areas are recruited during WM, they are recruited in a manner that resembles how these areas are used during perception.

Strengths:

Duan and Curtis very convincingly show that aperture effects that are present during perception, do not appear to be present during the working memory delay. Especially when the debate about "why can we decode orientations from human visual cortex" was in full swing, many may have quietly assumed this to be true (e.g., "the memory delay has no stimuli, and ergo no stimulus aperture effects"), but it is definitely not self-evident and nobody ever thought to test it directly until now. In addition to the clear absence of aperture effects during the delay, Duan and Curtis also show that when stimulus energy aligns with the carrier orientation, cross-generalization between perception and memory does work (which could explain why perception-to-memory cross-decoding also works). All in all, this is a clever manipulation, and I'm glad someone did it, and did it well.

Weaknesses:

There seems to be a major possible confound that prohibits strong conclusions about "abstractions" into "line-like" representation, which is spatial attention. What if subjects simply attend the endpoints of the carrier grating, or attend to the edge of the screen where the carrier orientation "intersects" in order to do the task? This may also result in reconstructions that have higher bold at areas close to the stimulus/screen edges along the carrier orientation. The question then would be if this is truly an "abstracted representation", or if subjects are merely using spatial attention to do the task.

Alternatively (and this reaches back to the "fine vs coarse" debate), another argument could be that during memory, what we are decoding is indeed fine-scale inhomogenous sampling of orientation preferences across many voxels. This is clearly not the most convincing argument, as the spatial reconstructions (e.g., Figure 3A and C) show higher BOLD for voxels with receptive fields that are aligned to the remembered orientation (which is in itself a form of coarse-scale bias), but could still play a role.

To conclude that the spatial reconstruction from the data indeed comes from a line-like representation, you'd need to generate modeled reconstructions of all possible stimuli and representations. Yes, Figure 4 shows that line results in a modeled spatial map that resembles the WM data, but many other stimuli might too, and some may better match the data. For example, the alternative hypothesis (attention to grating endpoints) may very well lead to a very comparable model output to the one from a line. However testing this would not suffice, as there may be an inherent inverse problem (with multiple stimuli that can lead to the same visual field model).

The main conclusion, and title of the paper, that visual working memories are abstractions of percepts, is therefore not supported. Subjects could be using spatial attention, for example. Furthermore, even if it is true that gratings are abstracted into lines, this form of abstraction would not generalize to any non-spatial feature (e.g., color cannot become a line, contrast cannot become a line, etc.), which means it has limited explanatory power.

We thank the reviewer for bringing up these excellent questions.

First, to test the alternative hypothesis of spatial attention, we fed a dot image into the image-computable model. We placed the dot where we suspect one might place their spatial attention, namely, at the edge of the stimulus that is tangent to the orientation of the grating. We generated the model response for three orientations and their combination by rotating and averaging. From Author response image 1 below, one can see that this model does not match the line-like representation we reported. Nonetheless, we would like to avoid making the argument that attention does not play a role. We strongly suspect that if one was attending to multiple places along a path that makes up a line, it would produce the results we observed. But there begins a circularity in the logic, where one cannot distinguish between attention to a line-like representation and a line of attention being the line-like representation.

Author response image 1.

Reconstruction maps for the dot image at the edge of 15°, 75°, 135°, and the combined across three orientation conditions.

Second, we remain agnostic to the question of whether fine-scale inhomogenous sampling of orientation selective neurons may drive some of the decoding results we report here. It is possible that our line-like representations are driven by neurons tuned to the sample orientation that have receptive fields that lie along the line. Here, we instead focus on testing the idea that WM decoding does not depend on aperture biases.

Finally, we agree with the reviewer that there is much more work to be done in this area. Our working hypothesis, that WM representations are abstractions of percepts, is admittedly based on Occam's razor and an appeal to efficient coding principles. We also agree that these results may not generalize to all forms of WM (eg, color). As always, there is a tradeoff between interpretability (visual spatial formats in retinotopically organized maps) and generalizability. Frankly, we have no idea how one might be able to test these ideas when subjects might be using the most common type of memory reformatting - linguistic representations, which are incredibly efficient.

Additional context:

The working memory and perception tasks are rather different. In this case, the perception task does not require the subject to process the carrier orientation (which is largely occluded, and possibly not that obvious without paying attention to it), but attention is paid to contrast. In this scenario, stimulus energy may dominate the signal. In the WM task, subjects have to work out what orientation is shown to do the task. Given that the sensory stimulus in both tasks is brief (1.5s during memory encoding, and 2.5s total in the perceptual task), it would be interesting to look at decoding (and reconstructions) for the WM stimulus epoch. If abstraction (into a line) happens in working memory, then this perceptual part of the task should still be susceptible to aperture biases. It allows the authors to show that it is indeed during memory (and not merely the task or attentional state of the subject) that abstraction occurs.

Again, this is an excellent question. We used a separate perceptual task instead of the stimulus epoch as control mainly for two reasons. First, we used a control task in which participants had to process the contrast, not orientation, of the grating because we were concerned that participants would reformat the grating into a line-like representation to make the judgments. To avoid this, we used a task similar to the one used when previous researchers first found the stimulus vignetting effect (Roth et al., 2018). Again, our main goal was to try to focus on the bottom-up visual features. Second, because of the sluggishness of the BOLD response, combined with our task design (ie, memory delay always followed the target stimulus), we cannot disentangle the visual and memory responses that co-exist at this epoch. Any result could be misleading.

What's also interesting is what happens in the passive perceptual condition, and the fact that spatial reconstructions for areas beyond V1 and V2 (i.e., V3, V3AB, and IPS0-1) align with (implied) grating endpoints, even when an angular modulator is used (Figure 3C). Are these areas also "abstracting" the stimulus (in a line-like format)?

We agree these findings are interesting and replicate what we found in our previous paper (Kwak & Curtis, Neuron, 2022). We believe that these results do imply that these areas indeed store a reformatted line-like WM representation that is not biased by vignetting. We would like to extend a note of caution, however, because the decoding results in the higher order areas (V3AB, IPS0-1, etc) are somewhat poor (especially in comparison to V1, V2, V3) (see Figure 2).

Reviewer #2:

Summary:

According to the sensory recruitment model, the contents of working memory (WM) are maintained by activity in the same sensory cortical regions responsible for processing perceptual inputs. A strong version of the sensory recruitment model predicts that stimulus-specific activity patterns measured in sensory brain areas during WM storage should be identical to those measured during perceptual processing. Previous research casts doubt on this hypothesis, but little is known about how stimulus-specific activity patterns during perception and memory differ. Through clever experimental design and rigorous analyses, Duan & Curtis convincingly demonstrate that stimulus-specific representations of remembered items are highly abstracted versions of representations measured during perceptual processing and that these abstracted representations are immune to aperture biases that contribute to fMRI feature decoding. The paper provides converging evidence that neural states responsible for representing information during perception and WM are fundamentally different, and provides a potential explanation for this difference.

Strengths:

(1) The generation of stimuli with matching vs. orthogonal orientations and aperture biases is clever and sets up a straightforward test regarding whether and how aperture biases contribute to orientation decoding during perception and WM. The demonstration that orientation decoding during perception is driven primarily by aperture bias while during WM it is driven primarily by orientation is compelling.

(2) The paper suggests a reason why orientation decoding during WM might be immune to aperture biases: by weighting multivoxel patterns measured during WM storage by spatial population receptive field estimates from a different task the authors show that remembered but not actively viewed - orientations form "line-like" patterns in retinotopic cortical space.

We thank the reviewer for noting the strengths in our work.

Weaknesses:

(1) The paper tests a strong version of the sensory recruitment model, where neural states representing information during WM are presumed to be identical to neural states representing the same information during perceptual processing. As the paper acknowledges, there is already ample reason to doubt this prediction (see, e.g., earlier work by Kok & de Lange, Curr Biol 2014; Bloem et al., Psych Sci, 2018; Rademaker et al., Nat Neurosci, 2019; among others). Still, the demonstration that orientation decoding during WM is immune to aperture biases known to drive orientation decoding during perception makes for a compelling demonstration.

We agree with the reviewer, and would add that the main problem with the sensory recruitment model of WM is that it remains underspecified. The work cited above and in our paper, and the results in this report is only the beginning of efforts to fully detail what it means to recruit sensory mechanisms for memory.

(2) Earlier work by the same group has reported line-like representations of orientations during memory storage but not during perception (e.g., Kwak & Curtis, Neuron, 2022). It's nice to see that result replicated during explicit perceptual and WM tasks in the current study, but I question whether the findings provide fundamental new insights into the neural bases of WM. That would require a model or explanation describing how stimulus-specific activation patterns measured during perception are transformed into the "line-like" patterns seen during WM, which the authors acknowledge is an important goal for future research.

We agree with the reviewer that perhaps some might see the current results as an incremental step given our previous paper. However, we would point out that researchers have been decoding memorized orientation from the early visual cortex for 15 years, and not one of those highly impactful studies had ever done what we did here, which was to test if decoded WM representations are the product of aperture biases. Not only do our results indicate that decoding memorized orientation is immune to these biases, but they critically suggest a reason why one can decode orientation during WM.

Reviewer #3:

Summary:

In this work, Duan and Curtis addressed an important issue related to the nature of working memory representations. This work is motivated by findings illustrating that orientation decoding performance for perceptual representations can be biased by the stimulus aperture (modulator). Here, the authors examined whether the decoding performance for working memory representations is similarly influenced by these aperture biases. The results provide convincing evidence that working memory representations have a different representational structure, as the decoding performance was not influenced by the type of stimulus aperture.

Strengths:

The strength of this work lies in the direct comparison of decoding performance for perceptual representations with working memory representations. The authors take a well-motivated approach and illustrate that perceptual and working memory representations do not share a similar representational structure. The authors test a clear question, with a rigorous approach and provide convincing evidence. First, the presented oriented stimuli are carefully manipulated to create orthogonal biases introduced by the stimulus aperture (radial or angular modulator), regardless of the stimulus carrier orientation. Second, the authors implement advanced methods to decode the orientation information present, in visual and parietal cortical regions, when directly perceiving or holding an oriented stimulus in memory. The data illustrates that working memory decoding is not influenced by the type of aperture, while this is the case in perception. In sum, the main claims are important and shed light on the nature of working memory representations.

We thank the reviewer for noting the strengths in our work.

Weaknesses:

I have a few minor concerns that, although they don't affect the main conclusion of the paper, should still be addressed.

(1) Theoretical framing in the introduction: Recent work has shown that decoding of orientation during perception does reflect orientation selectivity, and it is not only driven by the stimulus aperture (Roth, Kay & Merriam, 2022).

Excellent point, and similar to the point made by Reviewer 1. We now adjust our text and cite the paper in the Introduction.

Below, we paste our response to Reviewer 1:

“Second, we remain agnostic to the question of whether fine-scale inhomogenous sampling of orientation selective neurons may drive some of the decoding we report here. It is possible that our line-like representations are driven by neurons tuned to the sample orientation that have receptive fields that lie along the line. Here, we instead focus on testing the idea that WM decoding does not depend on aperture biases.”

(2) Figure 1C illustrates the principle of how the radial and angular modulators bias the contrast energy extracted by the V1 model, which in turn would influence orientation decoding. It would be informative if the carrier orientations used in the experiment were shown in this figure, or at a minimum it would be mentioned in the legend that the experiment used 3 carrier orientations (15{degree sign}, 75{degree sign}, 135{degree sign}) clockwise from vertical. Related, when trying to find more information regarding the carrier orientation, the 'Stimuli' section of the Methods incorrectly mentions that 180 orientations are used as the carrier orientation.

We apologize for not clearly indicating the stimulus features in the figure. Now, we added the information about the target orientations in Figure 1C legend. Also, we now corrected in the Methods section the mistakes about the carrier orientation and the details of the task. Briefly, participants were asked to use a continuous report over 180 orientations. We now clarify that “We generated 180 orientations for the carrier grating to cover the whole orientation space during the continuous report task.”

(3) The description of the image computable V1 model in the Methods is incomplete, and at times inaccurate. i) The model implements 6 orientation channels, which is inaccurately referred to as a bandwidth of 60{degree sign} (should be 180/6=30). ii) The steerable pyramid combines information across phase pairs to obtain a measure of contrast energy for a given stimulus. Here, it is only mentioned that the model contains different orientation and spatial scale channels. I assume there were also 2 phase pairs, and they were combined in some manner (squared and summed to create contrast energy). Currently, it is unclear what the model output represents. iii) The spatial scale channel with the maximal response differences between the 2 modulators was chosen as the final model output. What spatial frequency does this channel refer to, and how does this spatial frequency relate to the stimulus?

(i) First, we thank the reviewer for pointing out this mistake since the range of orientations should be 180deg instead of 360deg. We corrected this in the revised version.

(ii) Second, we apologize for not being clear. In the second paragraph of the “Simulate model outputs” section, we wrote,

“For both types of stimuli, we used three target orientations (15°, 75°, and 135° clockwise from vertical), which had two kinds of phases for both the carriers and the modulators. We first generated the model’s responses to each target image separately, then averaged the model responses across all phases for each orientation condition.”

We have corrected this text by now writing,

from vertical), two phases for the carrier (0 or π), and two phases for the modulator (sine “For both types of stimuli, we used three target orientations (15°, 75°, and 135° clockwise from vertical), two phases for the carrier (0 or π), and two phases for the modulator (sine or cosine phase). We first generated the model responses to each phase condition separately, then averaged them across all phases for each orientation condition.”

(iii) Third and again we apologize for the misunderstanding. Since both modulated gratings have the same spatial frequency, the channel with the largest response should be equal to the spatial frequency of the stimulus. We corrected this by now writing,

“For the final predicted responses, we chose the subband with maximal responses (the 9th level), which corresponds to the spatial frequency of the stimulus (Roth, Heeger, and Merriam 2018).”

(4) It is not clear from the Methods how the difficulty in the perceptual control task was controlled. How were the levels of task difficulty created?

Apologies for not being clear. The task difficulty was created by setting the contrast differences between the two stimuli. The easiest level is choosing the first and the last contrast as pairs, while the hardest level is choosing the continuous two contrasts. We added these sentences

“The contrast for each stimulus was generated from a predefined set of 20 contrasts uniformly distributed between 0.5 and 1.0 (0.025 step size). We created 19 levels of task difficulty based on the contrast distance between the two stimuli. Thus, the difficulty ranged from choosing contrast pairs with the largest difference (0.5, easiest) to contrast pairs with the smallest difference (0.025, hardest). Task difficulty level changed based on an adaptive, 1-up-2-down staircase procedure (Levitt 1971) to maintain performance at approximately 70% correct.”

Recommendations For The Authors

(Reviewer #1):

(1) If the black circle (Fig 3A & C) is the stimulus size, and the stimulus (12º) is roughly half the size of the entire screen (24.8º), then how are spatial reconstructions generated for parts of the visual field that fall outside of the screen? I am asking because in Figure 3 the area over which spatial reconstructions are plotted has a diameter at least 3 times the diameter of that black circle (the stimulus). I'm guessing this is maybe possible when using a very liberal fitting approach to prf's, where the center of a prf can be outside of the screen (so you'd fit a circle to an elongated blob, assuming that blob is the edge of a circle, or something). Can you really reliably estimate that far out into visual space/ extrapolate prf's that exist in a part of the space you did not fully map (because it's outside of the screen)?

We thank the reviewer for pointing out this confusing issue.

First, the spatial construction map has a diameter 3 times the diameter of the stimulus because we included voxels whose pRF eccentricities were within 20º in the reconstruction, the same as Kwak & Curtis, 2022. There are reasons for doing so. First, while the height of the screen is 24.8º, the width of the screen is 44º. Thus, it is possible to have voxels whose pRF eccentricities are >20º. Second, for areas outside the height boundaries, there might not be pRF centers, but the whole pRF Gaussian distributions might still cover the area. Moreover, when creating the final map combined across three orientation conditions, we rotated them to be centered vertically, which then required a 20x20º square. Finally, inspecting the reconstruction maps, we noticed that the area that was twice the stimulus size (black circle) made very little contributions to the reconstructions. Therefore, the results depicted in Figure 3A&C are justified, but see the next comment and our response.

(2) Is the quantification in 3B/C justified? The filter line uses a huge part of visual space outside of the stimulus (and even the screen). For the angular modulator in the "perception" condition, this means that there is no peak at -90/90 degree. But if you were to only use a line that is about the size of the stimulus (a reasonable assumption), it would have a peak at -90/90 degree.

This is an excellent question. We completely agree that it is more reasonable to use filter lines that have the same size (12º) as the stimulus instead of the whole map size (40º). Based on the feedback from the Reviewer, we redid the spatial reconstruction analyses and now include the following changes to Figure 3.

(1) We fitted the lines using pixels only within the stimulus. In Figure 3A and Figure 3C, we now replaced the reconstruction maps.

(2) We added the color bar in Figure 3A.

(3) We regenerated the filtered responses and calculated the fidelity results by using line filters with the stimulus size. We replaced the filtered responses and fidelity results in Figure 3B and Figure 3D. With the new analysis, as anticipated by the Reviewer, we now found peaks at -90/90 degrees for the angular modulated gratings in the perceptual control task in V1 and V2. Thank you Reviewer 1!!!!

(4) We also made corresponding changes in the Supplementary Figure S4 and S5, as well as the statistical results in Table S4 and S5.

(5) In the “Methods” section, we added “within the stimulus size” for both “fMRI data analysis: Spatial reconstruction” and “Quantification and statistical analysis” subsections.

(3) Figure 4 is nice, but not exactly quantitative. It does not address that the reconstructions from the perceptual task are hugging the stimulus edges much more closely compared to the modeled map. Conversely, the yellow parts of the reconstructions from the delay fan out much further than those of the model. The model also does not seem to dissociate radial/angular stimuli, while in the perceptual data the magnitude of perceptual reconstruction is clearly much weaker for angular compared to radial modulator.

We thank the reviewer for this question. First, we admit that Figure 4 is more qualitative than quantitative. However, we see no alternative that better depicts the similarity in the model prediction and the fMRI results for the perceptual control and WM tasks. The figure clearly shows the orthogonal aperture bias. Second, we agree that aspects of the observed fMRI results are not perfectly captured by the model. This could be caused by many reasons, including fMRI noise, individual differences, etc. Importantly, different modulators induce orthogonal aperture bias in the perceptual but not the WM task, and therefore does not have a major impact on the conclusions.

(4) The working memory and perception tasks are rather different. In this case, the perception task does not require the subject to process the carrier orientation (which is largely occluded, and possibly not that obvious without paying attention to it), but attention is paid to contrast. In this scenario, stimulus energy may dominate the signal. In the WM task, subjects have to work out what orientation is shown to do the task. Given that the sensory stimulus in both tasks is brief (1.5s during memory encoding, and 2.5s total in the perceptual task), it would be interesting to look at decoding (and reconstructions) for the WM stimulus epoch. If abstraction (into a line) happens in working memory, then this perceptual part of the task should still be susceptible to aperture biases. It allows the authors to show that it is indeed during memory (and not merely the task or attentional state of the subject) that abstraction occurs.

We addressed the same point in the response for Reviewer 1, “additional context” section.

Recommendations for improving the writing:

(1) The main text had too little information about the Methods. Of course, some things need not be there, but others are crucial to understanding the basics of what is being shown. For example, the main text does not describe how many orientations are used (well... actually the caption to Figure 1 says there are 2: horizontal and vertical, which is confusing), and I had to deduce from the chance level (1/3) that there must have been 3 orientations. Also, given how important the orthogonality of the carrier and modulator are, it would be good to have this explicit (I would even want an analysis showing that indeed the two are independent). A final example is the use of beta weights, and for delay period decoding only the last 6s (of the 12s delay) are modeled and used for decoding.

We thank the reviewer for identifying aspects of the manuscript that were confusing. We made several changes to the paper to clarify these details.

First, we added the information about the orientations we used in the caption for Figure 1 and made it clear that Figure 1C is just an illustration using vertical/horizontal orientations. Second, the carrier and the modulator are different in many ways. For example, the carrier is a grating with orientation and contrast information, while the modulator is the aperture that bounds the grating without these features. Their phases are orthogonal, and we added this in the second paragraph of the “Stimuli” section. Last, in the main text and the captions, we now denote “late delay” when writing about our procedures.

(2) Right under Figure 3, the text reads "angular modulated gratings produced line-like representations that were orthogonal carrier orientation reflecting the influence of stimulus vignetting", but the quantification (Figure 3D) does not support this (there is no orthogonal "bump" in the filtered responses from V1-V3, and one aligned with the carrier orientation in higher areas).

This point was addressed in the “recommendations for the authors (Reviewer 1), point 2” above.

Minor corrections to text and figures:

(1) Abstract: "are WM codes" should probably be "WM codes are".

We prefer to keep “are WM codes” as it is grammatically correct.

(2) Introduction: Second sentence 2nd paragraph: representations can be used to decode representations? Or rather voxel patterns can be used...

Changed to “On the one hand, WM representations can be decoded from the activity patterns as early as primary visual cortex (V1)...”

(3) Same paragraph: might be good to add more references to support the correlation between V1 decoding and behavior. There's an Ester paper, and Iamchinina et al. 2021. These are not trial-wise, but trial-wise can also be driven by fluctuating arousal effects, so across-subject correlations help fortify this point.

We added these two papers as references.

(4) Last paragraph: "are WM codes" should probably be "WM codes are".

See (1) above.

(5) Figure 1B & 2A caption: "stimulus presenting epoch" should probably be "stimulus presentation epoch".

Changed to “stimulus epoch”.

(6) Figure 1C: So this is very unclear, to say stimuli are created using vertical and horizontal gratings (when none of the stimuli used in the experiment are either).

We solved and answered this point in response to Reviewer 3, point 2.

(7) Figure 2B caption "cross" should probably be "across".

We believe “cross” is fine since cross here means cross-decoding.

(8) Figure 3A and C are missing a color bar, so it's unclear how these images are generated (are they scaled, or not) and what the BOLD values are in each pixel.

All values in the map were scaled to be within -1 to 1. We added the color bar in both Figure 3 and Figure 4.

(9) Figure 3B and D (bottom row) are missing individual subject data.

We use SEM to indicate the variance across subjects.

(10) Figure D caption: "early (V1 and V2)" should probably be "early areas (V1 and V2)".

Corrected.

(11) Methods, stimuli says "We generated 180 orientations for the carrier grating to cover the whole orientation space." But it looks like only 3 orientations were generated, so this is confusing.

We solved and answered this point in response to Reviewer 3, point 2.

(12) Further down (fMRI task) "random jitters" is probably "random jitter"

Corrected.

Author response:

Response to Reviewer #1 (Public Review):

We thank the reviewer for their constructive criticism of our study, their proposed solutions, and for highlighting areas of the methodology and analytical pipeline where explanations were unclear or unsatisfactory. We will take the reviewer’s feedback into account to improve the clarity and readability of the revised manuscript. We acknowledge the importance of ruling out eye movements as a potential confound. We address these concerns briefly below, but a more detailed explanation (and a full breakdown of the relevant analyses, including the corrected and uncorrected results) will be provided in the revised manuscript.

First, the source of EEG activity recorded from the frontal electrodes is often unclear. Without an external reference, it is challenging to resolve the degree to which frontal EEG activity represents neural or muscular responses1. Thus, as a preventative measure against the potential contribution of eye movement activity, for all our EEG analyses, we only included activity from occipital, temporal, and parietal electrodes (the selected electrodes can be seen in the final inset of Figure 3).

Second, as suggested by the reviewer, we re-ran our analyses using the activity measured from the frontal electrodes alone. If the source of the nonlinear decoding accuracy in the AV condition was muscular activity produced by eye movements, we would expect to observe better decoding accuracy from sensors closer to the source. Instead, we found that decoding accuracy from the frontal electrodes (peak d' = 0.08) was less than half that of decoding accuracy from the more posterior electrodes (peak d' = 0.18). These results suggest that the source of neural activity containing information about stimulus position was located over occipito-parietal areas, consistent with our topographical analyses (inset of Figure 4).

Third, we compared the average eye movements between the three main sensory conditions (auditory, visual, and audiovisual). In the visual condition, there was little difference in eye movements corresponding to the five stimulus locations, likely because the visual stimuli were designed to be spatially diffuse. For the auditory and audiovisual conditions, there was more distinction between eye movements corresponding to the stimulus locations. However, these appeared to be the same between auditory and audiovisual conditions. If consistent saccades to audiovisual stimuli had been responsible for the nonlinear decoding we observed, we would expect to find a higher positive correlation between horizontal eye position and stimulus location in the audiovisual condition than in the auditory or visual conditions. Instead, we found no difference in correlation between audiovisual and auditory stimuli, indicating that eye movements were equivalent in these conditions and unlikely to explain better decoding accuracy for audiovisual stimuli.

Finally, we note that the stricter eye movement criterion acknowledged in the Discussion section of the original manuscript resulted in significantly better audiovisual d' than the MLE prediction, but this difference did not survive cluster correction. This is an important distinction to make as, when combined with the results described above, it seems to support our original interpretation that the stricter criterion combined with our conservative measure of (mass-based) cluster correction2 led to type 2 error.

References

(1) Roy, R. N., Charbonnier, S., & Bonnet, S. (2014). Eye blink characterization from frontal EEG electrodes using source separation and pattern recognition algorithms. Biomedical Signal Processing and Control, 14, 256–264.

(2) Pernet, C. R., Latinus, M., Nichols, T. E., & Rousselet, G. A. (2015). Cluster-based computational methods for mass univariate analyses of event-related brain potentials/fields: A simulation study. Journal of Neuroscience Methods, 250, 85–93.

Response to Reviewer #2 (Public Review):

We thank the reviewer for their insight and constructive feedback. As emphasized in the review, an interesting question that arises from our results is that, if the neural data exceeds the optimal statistical decision (MLE d'), why doesn’t the behavioural data? We agree with the reviewer’s suggestion that more attention should be devoted to this question, and plan to provide a deeper discussion of the relationship between behavioural and neural super-additivity in the revised manuscript. We also note that while this discrepancy remains unexplained, our results are consistent with the literature. That is, both non-linear neural responses (single-cell recordings) and behavioural responses that match MLE are reliable phenomenon in multisensory integration1,2,3,4.

One possible explanation for this puzzling discrepancy is that behavioural responses occur sometime after the initial neural response to sensory input. There are several subsequent neural processes between perception and a behavioural response5, all of which introduce additional noise that may obscure super-additive perceptual sensitivity. In particular, the mismatch between neural and behavioural accuracy may be the result of additional neural processes that translate sensory activity into a motor response to perform the behavioural task.

Our measure of neural super-additivity (exceeding optimally weighted linear summation) differs from how it is traditionally assessed (exceeding summation of single neuron responses)2. However, neither method has yet fully explained how this neural activity translates to behavioural responses, and we think that more work is needed to resolve the abovementioned discrepancy. However, our method will facilitate this work by providing a reliable method of measuring neural super-additivity in humans, using non-invasive recordings.

References

(1) Alais, D., & Burr, D. (2004). The ventriloquist effect results from near-optimal bimodal integration. Current Biology, 14(3), 257–262.

(2) Ernst, M. O., & Banks, M. S., (2002). Humans integrate visual and haptic information in a statistically optimal fashion. Nature, 415(6870), 429–433.

(3) Meredith, M. A., & Stein, B. E. (1993). Interactions among converging sensory inputs in the superior colliculus. Science, 221, 389–391.

(4) Stanford, T. R., & Stein, B. E. (2007). Superadditivity in multisensory integration: putting the computation in context. Neuroreport 18, 787–792.

(5) Heekeren, H., Marrett, S. & Ungerleider, L. (2008). The neural systems that mediate human perceptual decision making. Nature Reviews Neuroscience, 9, 467–479.

Author response:

Thanks for the eLife assessment

“This study employed a comprehensive approach to examining how the MT+ region integrates into a complex cognition system in mediating human visuo-spatial intelligence. While the findings are useful, the experimental evidence is incomplete and the study design, hypothesis, analyses, writing, and presentation need to be improved.” We plan to revise the manuscript according to the comments of Public Reviews.

We are grateful for the excellent and very helpful comments, and now we address provisional author responses.

Reviewer #1 (Public Review):

Summary:

The study of human intelligence has been the focus of cognitive neuroscience research, and finding some objective behavioral or neural indicators of intelligence has been an ongoing problem for scientists for many years. Melnick et al, 2013 found for the first time that the phenomenon of spatial suppression in motion perception predicts an individual's IQ score. This is because IQ is likely associated with the ability to suppress irrelevant information. In this study, a high-resolution MRS approach was used to test this theory. In this paper, the phenomenon of spatial suppression in motion perception was found to be correlated with the visuo-spatial subtest of gF, while both variables were also correlated with the GABA concentration of MT+ in the human brain. In addition, there was no significant relationship with the excitatory transmitter Glu. At the same time, SI was also associated with MT+ and several frontal cortex FCs.

Strengths:

(1) 7T high-resolution MRS is used.

(2) This study combines the behavioral tests, MRS, and fMRI.

Weaknesses:

(1) In the intro, it seems to me that the multiple-demand (MD) regions are the key in this study. However, I didn't see any results associated with the MD regions. Did I miss something??

Thank reviewer for pointing this out. After careful consideration, we agree with your point of view. According to the results of Melnick 2013, the motion surround suppression (SI) and the time thresholds of small and large gratings representing hMT+ functionality are correlated with Verbal Comprehension, Perceptual Reasoning, Working Memory, and Processing Speed Indicators, with correlation coefficients of 0.69, 0.47, 0.49, and 0.50, respectively. This suggests that hMT+ does have the potential to become the core of MD system. However, due to our results only delving into “the GABA-ergic inhibition in human MT predicts visuo-spatial intelligence mediated by reverberation with frontal cortex”, it is not yet sufficient to prove that hMT+is the core node of the MD system, we will adjust the explanatory logic of the article, that is, emphasizing the de-redundancy of hMT+ in visual-spatial intelligence and the improvement of information processing efficiency, while weakening the significance of hMT+ in MD systems.

(2) How was the sample size determined? Is it sufficient??

Thank reviewer for pointing this out. We use G*power to determine our sample size. In the study by Melnick (2013), they reported a medium effect between SI and Perception Reasoning sub-ability (r=0.47). Here we use this r value as the correlation coefficient (ρ H1), setting the power at the commonly used threshold of 0.8 and the alpha error probability at 0.05. The required sample size is calculated to be 26. This ensures that our study has adequate power to yield valid statistical results. Furthermore, compared to earlier within-subject studies like Schallmo et al.'s 2018 research, which used 22 datasets to examine GABA levels in MT+ and the early visual cortex (EVC), our study includes a more extensive dataset.

(3) In Schallmo elife 2018, there was no correlation between GABA concentration and SI. How can we justify the different results different here?

Thank reviewer for pointing this out. There are several differences between us:

a. While the earlier study by Schallmo et al. (2018) employed 3T MRS, we utilize 7T MRS, enhancing our ability to detect and measure GABA with greater accuracy.

b. Schallmo elife 2018 choose to use the bilateral hMT+ as the MRS measurement region while we use the left hMT+. The reason why we focus on left hMT+ are describe in reviewer 1. (6). Briefly, use of left MT/V5 as a target was motivated by studies demonstrating that left MT/V5 TMS is more effective at causing perceptual effects (Tadin et al., 2011).

c. The resolution of MRS sequence in Schallmo elife 2018 is 3 cm isotropic voxel, while we apply 2 cm isotropic voxel. This helps us more precisely locate hMT+ and exclude more white matter signal.

(4) Basically this study contains the data of SI, BDT, GABA in MT+ and V1, Glu in MT+ and V1-all 6 measurements. There should be 6x5/2 = 15 pairwise correlations. However, not all of these results are included in Figure 1 and supplementary 1-3. I understand that it is not necessary to include all figures. But I suggest reporting all values in one Table.

We thank the reviewer for the good suggestion, we are planning to make a correlation matrix to reporting all values.

(5) In Melnick (2013), the IQ scores were measured by the full set of WAIS-III, including all subtests. However, this study only used the visual spatial domain of gF. I wonder why only the visuo-spatial subtest was used not the full WAIS-III?

We thank the reviewer for pointing this out. The decision was informed by Melnick’s findings which indicated high correlations between Surround suppression (SI) and the Verbal Comprehension, Perceptual Reasoning, Working Memory, and Processing Speed Indexes, with correlation coefficients of 0.69, 0.47, 0.49, and 0.50, respectively. It is well-established that the hMT+ region of the brain is a sensory cortex involved in visual perception processing (3D perception). Furthermore, motion surround suppression (SI), a specific function of hMT+, aligns closely with this region's activities. Given this context, the Perception Reasoning sub-ability was deemed to have the clearest mechanism for further exploration. Consequently, we selected the most representative subtest of Perception Reasoning—the Block Design Test—which primarily assesses 3D visual intelligence.

(6) In the functional connectivity part, there is no explanation as to why only the left MT+ was set to the seed region. What is the problem with the right MT+?

We thank the reviewer for pointing this out. The main reason is that our MRS ROI is the left hMT+, we would like to make different models’ ROI consistent to each other. Use of left MT/V5 as a target was motivated by studies demonstrating that left MT/V5 TMS is more effective at causing perceptual effects (Tadin et al., 2011). In addition, we will check the results of our localizer to confirm whether similar findings are consistently replicated.

(7) In Melnick (2013), the authors also reported the correlation between IQ and absolute duration thresholds of small and large stimuli. Please include these analyses as well.

We thank the reviewer for the good advice. Containing such result do help researchers compare the result between Melnick and us. We are planning to make such picture in the revised version.

Reviewer #2 (Public Review):

Summary:

Recent studies have identified specific regions within the occipito-temporal cortex as part of a broader fronto-parietal, domain-general, or "multiple-demand" (MD) network that mediates fluid intelligence (gF). According to the abstract, the authors aim to explore the mechanistic roles of these occipito-temporal regions by examining GABA/glutamate concentrations. However, the introduction presents a different rationale: investigating whether area MT+ specifically, could be a core component of the MD network.

Strengths:

The authors provide evidence that GABA concentrations in MT+ and its functional connectivity with frontal areas significantly correlate with visuo-spatial intelligence performance. Additionally, serial mediation analysis suggests that inhibitory mechanisms in MT+ contribute to individual differences in a specific subtest of the Wechsler Adult Intelligence Scale, which assesses visuo-spatial aspects of gF.

Weaknesses:

(1) While the findings are compelling and the analyses robust, the study's rationale and interpretations need strengthening. For instance, Assem et al. (2020) have previously defined the core and extended MD networks, identifying the occipito-temporal regions as TE1m and TE1p, which are located more rostrally than MT+. Area MT+ might overlap with brain regions identified previously in Fedorenko et al., 2013, however the authors attribute these activations to attentional enhancement of visual representations in the more difficult conditions of their tasks. For the aforementioned reasons, It is unclear why the authors chose MT+ as their focus. A stronger rationale for this selection is necessary and how it fits with the core/extended MD networks.

We really appreciate reviewer’s opinions. The reason why we focus on hMT+ is following: According to the results of Melnick 2013, the motion surround suppression (SI) and the time thresholds of small and large gratings representing hMT+ functionality are correlated with Verbal Comprehension, Perceptual Reasoning, Working Memory, and Processing Speed Indicators, with high correlation coefficients of 0.69, 0.47, 0.49, and 0.50, respectively. In addition, Fedorenko et al. 2013, the averaged MD activity region appears to overlap with hMT+. Based on these findings, we assume that hMT+ does have the potential to become the core of MD system.

(2) Moreover, although the study links MT+ inhibitory mechanisms to a visuo-spatial component of gF, this evidence alone may not suffice to position MT+ as a new core of the MD network. The MD network's definition typically encompasses a range of cognitive domains, including working memory, mathematics, language, and relational reasoning. Therefore, the claim that MT+ represents a new core of MD needs to be supported by more comprehensive evidence.

Thank reviewer for pointing this out. After careful consideration, we agree with your point of view. Due to our results only delving into visuo-spatial intelligence, it is not yet sufficient to prove that hMT is the core node of the MD system. We will adjust the explanatory logic of the article, that is, emphasizing the de-redundancy of hMT+in visual-spatial intelligence and the improvement of information processing efficiency, while weakening the significance of hMT+ in MD systems.

Reviewer #3 (Public Review):

Summary:

This manuscript aims to understand the role of GABA-ergic inhibition in the human MT+ region in predicting visuo-spatial intelligence through a combination of behavioral measures, fMRI (for functional connectivity measurement), and MRS (for GABA/glutamate concentration measurement). While this is a commendable goal, it becomes apparent that the authors lack fundamental understanding of vision, intelligence, or the relevant literature. As a result, the execution of the research is less coherent, dampening the enthusiasm of the review.

Strengths:

(1) Comprehensive Approach: The study adopts a multi-level approach, i.e., neurochemical analysis of GABA levels, functional connectivity, and behavioral measures to provide a holistic understanding of the relationship between GABA-ergic inhibition and visuo-spatial intelligence.

(2) Sophisticated Techniques: The use of ultra-high field magnetic resonance spectroscopy (MRS) technology for measuring GABA and glutamate concentrations in the MT+ region is a recent development.

Weaknesses:

Study Design and Hypothesis

(1) The central hypothesis of the manuscript posits that "3D visuo-spatial intelligence (the performance of BDT) might be predicted by the inhibitory and/or excitation mechanisms in MT+ and the integrative functions connecting MT+ with the frontal cortex." However, several issues arise:

(1.1) The Suppression Index depicted in Figure 1a, labeled as the "behavior circle," appears irrelevant to the central hypothesis.

We thank the reviewer for pointing this out. In our study, the inhibitory mechanisms in hMT+ are conceptualized through two models: the neurotransmitter model and the behavior model. The Suppression Index is essential for elucidating the local inhibitory mechanisms within behavior model. However, we acknowledge that our initial presentation in the introduction may not have clearly articulated our hypothesis, potentially leading to misunderstandings. We plan to revise the introduction to better clarify these connections and ensure the relevance of the Suppression Index is comprehensively understood.

(1.2) The construct of 3D visuo-spatial intelligence, operationalized as the performance in the Block Design task, is inconsistently treated as another behavioral task throughout the manuscript, leading to confusion.

We thank the reviewer for pointing this out. We acknowledge that our manuscript may have inconsistently presented this construct across different sections, causing confusion. To address this, we plan to ensure a consistent description of 3D visuo-spatial intelligence in both the introduction and the discussion sections. But we would like to maintain 'Block Design task score' within the results section to help readers clarify which subtest we use.

(1.3) The schematics in Figure 1a and Figure 6 appear too high-level to be falsifiable. It is suggested that the authors formulate specific and testable hypotheses and preregister them before data collection.

We thank the reviewer for pointing this out. We are planning to revise the Figure 1a and make it less abstract and more logical. For Figure 6, the schematic represents our theoretical framework of how hMT+ works in the 3D viso-spatial intelligence, we believe the elements within this framework are grounded in related theories and supported by evidence discussed in our results and discussions section, making them specific and testable.

(2) Central to the hypothesis and design of the manuscript is a misinterpretation of a prior study by Melnick et al. (2013). While the original study identified a strong correlation between WAIS (IQ) and the Suppression Index (SI), the current manuscript erroneously asserts a specific relationship between the block design test (from WAIS) and SI. It should be noted that in the original paper, WAIS comprises Similarities, Vocabulary, Block design, and Matrix reasoning tests in Study 1, while the complete WAIS is used in Study 2. Did the authors conduct other WAIS subtests other than the block design task?

Thanks for pointing this out. Reviewer #1 also asked this question, we copy the answers in here “The decision was informed by Melnick’s findings which indicated high correlations between Surround suppression (SI) and the Verbal Comprehension, Perceptual Reasoning, Working Memory, and Processing Speed Indexes, with correlation coefficients of 0.69, 0.47, 0.49, and 0.50, respectively. It is well-established that the hMT+ region of the brain is a sensory cortex involved in visual perception processing (3D perception). Furthermore, motion surround suppression (SI), a specific function of hMT+, aligns closely with this region's activities. Given this context, the Perception Reasoning sub-ability was deemed to have the clearest mechanism for further exploration. Consequently, we selected the most representative subtest of Perception Reasoning—the Block Design Test—which primarily assesses 3D visual intelligence.”

(3) Additionally, there are numerous misleading references and unsubstantiated claims throughout the manuscript. As an example of misleading reference, "the human MT ... a key region in the multiple representations of sensory flows (including optic, tactile, and auditory flows) (Bedny et al., 2010; Ricciardi et al., 2007); this ideally suits it to be a new MD core." The two references in this sentence are claims about plasticity in the congenitally blind with sensory deprivation from birth, which is not really relevant to the proposal that hMT+ is a new MD core in healthy volunteers.

Thanks for pointing this out. We have carefully read the corresponding references and considered the corresponding theories and agree with these comments. Due to our results only delving into “the GABA-ergic inhibition in human MT predicts visuo-spatial intelligence mediated by reverberation with frontal cortex”, it is not yet sufficient to prove that hMT+ is the core node of the MD system, we will adjust the explanatory logic of the article, that is, emphasizing the de redundancy of hMT+in visual-spatial intelligence and the improvement of information processing efficiency, while weakening the significance of hMT+ in MD systems. In addition, regarding the potential central role of hMT+ in the MD system, we agree with your view that research on hMT+ as a multisensory integration hub mainly focuses on developmental processes. Meanwhile, in adults, the MST region of hMT+ is considered a multisensory integration area for visual and vestibular inputs, which potentially supports the role of hMT+ in multitasking multisensory systems (Gu et al., J. Neurosci, 26(1), 73–85, 2006; Fetsch et al., Nat. Neurosci, 15, 146–154, 2012.). Further research could explore how other intelligence sub-ability such as working memory and language comprehension are facilitated by hMT+'s features.

Another example of unsubstantiated claim: the rationale for selecting V1 as the control region is based on the assertion that "it mediates the 2D rather than 3D visual domain (Born & Bradley, 2005)". That's not the point made in the Born & Bradley (2005) paper on MT. It's crucial to note that V1 is where the initial binocular convergence occurs in cortex, i.e., inputs from both the right and left eyes to generate a perception of depth.

Thank you for pointing this out. We acknowledge the inappropriate citation of "Born & Bradley, 2005," which focuses solely on the structure and function of the visual area MT. However, we believe that choosing hMT+ as the domain for 3D visual analysis and V1 as the control region is justified. Cumming and DeAngelis (Annu Rev Neurosci, 24:203–238.2001) state that binocular disparity provides the visual system with information about the three-dimensional layout of the environment, and the link between perception and neuronal activity is stronger in the extrastriate cortex (especially MT) than in the primary visual cortex(V1). This supports our choice and emphasizes the relevance of MT+ in our study. We will revise our reference in the revised version.

Results & Discussion

(1) The missing correlation between SI and BDT is crucial to the rest of the analysis. The authors should discuss whether they replicated the pattern of results from Melnick et al. (2013) despite using only one WAIS subtest.

We thank for reviewer’s suggestion. Now the correlation result is placed in the supplemental material, we will put it back to the main text.

(2) ROIs: can the authors clarify if the results are based on bilateral MT+/V1 or just those in the left hemisphere? Can the authors plot the MRS scan area in V1? I would be surprised if it's precise to V1 and doesn't spread to V2/3 (which is fine to report as early visual cortex).

We thank for reviewer’s suggestion. We plan to draw the V1 ROI MRS scanning area and use the visual template to check if the scanning area contains V2/3. If it does, we will refer to it as the early visual cortex rather than specifically V1 in our reporting.

(3) Did the authors examine V1 FC with either the frontal regions and/or whole brain, as a control analysis? If not, can the author justify why V1 serves as the control region only in the MRS but not in FC (Figure 4) or the mediation analysis (Figure 5)? That seems a little odd given that control analyses are needed to establish the specificity of the claim to MT+

We thank for reviewer’s suggestion. We plan to do the V1 FC-behavior connection as control analysis. For mediation analysis, since V1 GABA/Glu has no correlation with BDT score, it is not sufficient to apply mediation analysis.

(4) It is not clear how to interpret the similarity or difference between panels a and b in Figure 4.

We thank reviewer for pointing this out. We plan to further interpret the difference between a and b in the revised version. Panels a represents BDT score correlated hMT+-region FC, which is obviously involved in frontal cortex. While panels b represents SI correlated hMT+-region FC, which shows relatively less regions. The overlap region is what we are interested in and explain how local inhibitory mechanisms works in the 3D viso-spatial intelligence. In addition, we would like to revise Figure 4 and point out the overlap region.

(5) SI is not relevant to the authors‘ priori hypothesis, but is included in several mediation analyses. Can the authors do model comparisons between the ones in Figure 5c, d, and Figure S6? In other words, is SI necessary in the mediation model? There seem discrepancies between the necessity of SI in Figures 5c/S6 vs. Figure 5d.

We thank the reviewer for highlighting this point. The relationship between the Suppression Index (SI) and our a priori hypotheses is elaborated in the response to reviewer 3, section (1). SI plays a crucial role in explicating how local inhibitory mechanisms function within the context of the 3D visuo-spatial task. Additionally, Figure 5c illustrates the interaction between the frontal cortex and hMT+, showing how the effects from the frontal cortex (BA46) on the Block Design Task are fully mediated by SI. This further underscores the significance of SI in our model.

(6) The sudden appearance of "efficient information" in Figure 6, referring to the neural efficiency hypothesis, raises concerns. Efficient visual information processing occurs throughout the visual cortex, starting from V1. Thus, it appears somewhat selective to apply the neural efficiency hypothesis to MT+ in this context.

We thank the reviewer for highlighting this point. There is no doubt that V1 involved in efficient visual information processing. However, in our result, the V1 GABA has no significant correlation between BDT score, suggesting that the V1 efficient processing might not sufficiently account for the individual differences in 3D viso-spatial intelligence. Additionally, we will clarify our use of the neural efficiency hypothesis by incorporating it into the introduction of our paper to better frame our argument.

Transparency Issues:

(1) Don't think it's acceptable to make the claim that "All data needed to evaluate the conclusions in the paper are present in the paper and/or the Supplementary information". It is the results or visualizations of data analysis, rather than the raw data themselves, that are presented in the paper/supp info.

We thank reviewer for pointing this out. We realized that such expression will lead to confusion. We will delete this expression.

(2) No GitHub link has been provided in the manuscript to access the source data, which limits the reproducibility and transparency of the study.

We thank reviewer for pointing this out. We will attach the GitHub link in the revised version.

Minor:

"Locates" should be replaced with "located" throughout the paper. For example: "To investigate this issue, this study selects the human MT complex (hMT+), a region located at the occipito-temporal border, which represents multiple sensory flows, as the target brain area."

We thank reviewer for pointing this out. We will revise it.

Use "hMT+" instead of "MT+" to be consistent with the term in the literature.

We thank reviewer for pointing this out. We agree to use hMT+ in the literature.

"Green circle" in Figure 1 should be corrected to match its actual color.

We thank reviewer for pointing this out. We will revise it.

The abbreviation for the Wechsler Adult Intelligence Scale should be "WAIS," not "WASI."

We thank reviewer for pointing this out. We will revise it.

Author Response:

We appreciate the thorough comments from the reviewers. Before revising the manuscript, we would like to briefly reply to the main concerns raised:

• Is pupil size a reliable proxy of effort? A vast amount of work demonstrates that pupil size sensitively scales with fluctuations in effort: for instance, the pupil dilates when increasing load in working memory, or multiple object tracking tasks, and such pupillary effects robustly explain individual differences in cognitive ability and fluctuations in performance across trials.1–4 This extends to the planning of movements as pupil dilations are observed prior to the execution of (eye) movements.5 As reviewed previously6–12 (based on vast literature each), any increase in effort is associated with an increase in pupil size. Inadvertently, we phrased as if the link between effort and pupil size was established via shared neural correlates. However, this is not the case as the link between effort and pupil size had been established well before the underlying neural circuitry of this relationship was investigated in detail. During the revision, we plan to rewrite this section to clarify that pupil size indexes effort and to provide a clear distinction between this link and putative neural underpinnings of such effort-linked modulations.

• Is saccade latency an alternative explanation for the link between effort and saccade selection? Longer saccade latencies may imply more complex oculomotor programming (e.g. saccades with larger amplitudes require longer latencies for non-microsaccades13, and latencies increase when distractors are presented14), and latencies are indeed known to differ across directions15,16. As suggested, it is possible that saccade latencies may also predict saccade preferences. However, even if this is the case, this would not constitute an alternative explanation. As saccade latency may index oculomotor programming complexity, it can potentially be considered an alternative outcome measure of effort, albeit restricted to the context of saccades. Therefore, if saccade latencies predict saccade preferences, this would not affect our conclusion, rather it would constitute as converging evidence that supports the conclusion that effort drives saccade selection.

A related question is why one would use pupil size as a measure of effort, given the methodological care that pupillometry requires. There are a number of points that make pupil size sensible and promising in comparison with saccade latencies. In contrast to saccade latencies, pupil size allows to capture the effort of different effector systems (e.g. head or hand movements), and potentially even the effort associated with covert shifts of attention. Moreover, pupil size is a temporally rich and continuous measure that allows to isolate processes unfolding prior to (eye) movement onset (e.g. oculomotor programming). Together, this makes pupil size a powerful tool to study the costs of visual selection more broadly. In the revision, we will add analyses incorporating latencies and other other saccade metrics. We will also discuss the differences between pupil size and saccade latencies in capturing saccade costs and effort.

• Are the current results causal or correlational? Most of the currently reported results are indeed correlational in nature. In our first tasks, we correlated pupil size during saccade planning to saccade preferences in a subsequent task. Although the link between across tasks was correlational, the observed relationship clearly followed our previously specified hypothesis.17 Moreover, experiments 1 and 2 of the visual search data replicated and extended this relationship. We also directly manipulated cognitive demand in the second visual search experiment. In line with the hypothesis that effort affects saccade selection, participants executed less saccades overall when performing a (primary) auditory dual task, and even cut the costly saccades most. Whilst mostly correlational, we do not know of a more fitting and parsimonious explanation for our findings than effort predicting saccade selection. We will address causality in the discussion for transparency and point more clearly to the second visual search experiment for causal evidence.

References

(1) Alnæs, D. et al. Pupil size signals mental effort deployed during multiple object tracking and predicts brain activity in the dorsal attention network and the locus coeruleus. J. Vis. 14, 1 (2014).

(2) Koevoet, D., Strauch, C., Van der Stigchel, S., Mathôt, S. & Naber, M. Revealing visual working memory operations with pupillometry: Encoding, maintenance, and prioritization. WIREs Cogn. Sci. e1668 (2023) doi:10.1002/wcs.1668.

(3) Robison, M. K. & Unsworth, N. Pupillometry tracks fluctuations in working memory performance. Atten. Percept. Psychophys. 81, 407–419 (2019).

(4) Unsworth, N. & Miller, A. L. Individual Differences in the Intensity and Consistency of Attention. Curr. Dir. Psychol. Sci. 30, 391–400 (2021).

(5) Richer, F. & Beatty, J. Pupillary Dilations in Movement Preparation and Execution. Psychophysiology 22, 204–207 (1985).

(6) Bumke, O. Die Pupillenstörungen Bei Geistes-Und Nervenkrankheiten. (Fischer, 1911).

(7) Kahneman, D. Attention and Effort. (Prentice-Hall, 1973).

(8) van der Wel, P. & van Steenbergen, H. Pupil dilation as an index of effort in cognitive control tasks: A review. Psychon. Bull. Rev. 25, 2005–2015 (2018).

(9) Loewenfeld, I. E. Mechanisms of reflex dilatation of the pupil. Doc. Ophthalmol. 12, 185–448 (1958).

(10) Mathôt, S. Pupillometry: Psychology, Physiology, and Function. J. Cogn. 1, 16 (2018).

(11) Sirois, S. & Brisson, J. Pupillometry. WIREs Cogn. Sci. 5, 679–692 (2014).

(12) Strauch, C., Wang, C.-A., Einhäuser, W., Van der Stigchel, S. & Naber, M. Pupillometry as an integrated readout of distinct attentional networks. Trends Neurosci. 45, 635–647 (2022).

(13) Kalesnykas, R. P. & Hallett, P. E. Retinal eccentricity and the latency of eye saccades. Vision Res. 34, 517–531 (1994).

(14) Walker, R., Deubel, H., Schneider, W. X. & Findlay, J. M. Effect of Remote Distractors on Saccade Programming: Evidence for an Extended Fixation Zone. J. Neurophysiol. 78, 1108–1119 (1997).

(15) Hanning, N. M., Himmelberg, M. M. & Carrasco, M. Presaccadic attention enhances contrast sensitivity, but not at the upper vertical meridian. iScience 25, 103851 (2022).

(16) Hanning, N. M., Himmelberg, M. M. & Carrasco, M. Presaccadic Attention Depends on Eye Movement Direction and Is Related to V1 Cortical Magnification. J. Neurosci. 4

4, (2024).

(17) Koevoet, D., Strauch, C., Naber, M. & Van der Stigchel, S. The Costs of Paying Overt and Covert Attention Assessed With Pupillometry. Psychol. Sci. 34, 887–898 (2023).

Author response:

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

Public Reviews:

We thank the reviewers for the detailed assessment of our work as well as their praise and constructive feedback which helped us to significantly improve our manuscript.

Reviewer #1 (Public Review):

The inferior colliculus (IC) is the central auditory system's major hub. It integrates ascending brainstem signals to provide acoustic information to the auditory thalamus. The superficial layers of the IC ("shell" IC regions as defined in the current manuscript) also receive a massive descending projection from the auditory cortex. This auditory cortico-collicular pathway has long fascinated the hearing field, as it may provide a route to funnel "high-level" cortical signals and impart behavioral salience upon an otherwise behaviorally agnostic midbrain circuit.

Accordingly, IC neurons can respond differently to the same sound depending on whether animals engage in a behavioral task (Ryan and Miller 1977; Ryan et al., 1984; Slee & David, 2015; Saderi et al., 2021; De Franceschi & Barkat, 2021). Many studies also report a rich variety of non-auditory responses in the IC, far beyond the simple acoustic responses one expects to find in a "low-level" region (Sakurai, 1990; Metzger et al., 2006; Porter et al., 2007). A tacit assumption is that the behaviorally relevant activity of IC neurons is inherited from the auditory cortico-collicular pathway. However, this assumption has never been tested, owing to two main limitations of past studies:

(1) Prior studies could not confirm if data were obtained from IC neurons that receive monosynaptic input from the auditory cortex.

(2) Many studies have tested how auditory cortical inactivation impacts IC neuron activity; the consequence of cortical silencing is sometimes quite modest. However, all prior inactivation studies were conducted in anesthetized or passively listening animals. These conditions may not fully engage the auditory cortico-collicular pathway. Moreover, the extent of cortical inactivation in prior studies was sometimes ambiguous, which complicates interpreting modest or negative results.

Here, the authors' goal is to directly test if auditory cortex is necessary for behaviorally relevant activity in IC neurons. They conclude that surprisingly, task relevant activity in cortico-recipient IC neuron persists in absence of auditory cortico-collicular transmission. To this end, a major strength of the paper is that the authors combine a sound-detection behavior with clever approaches that unambiguously overcome the limitations of past studies.

First, the authors inject a transsynaptic virus into the auditory cortex, thereby expressing a genetically encoded calcium indicator in the auditory cortex's postsynaptic targets in the IC. This powerful approach enables 2-photon Ca2+ imaging from IC neurons that unambiguously receive monosynaptic input from auditory cortex. Thus, any effect of cortical silencing should be maximally observable in this neuronal population. Second, they abrogate auditory cortico-collicular transmission using lesions of auditory cortex. This "sledgehammer" approach is arguably the most direct test of whether cortico-recipient IC neurons will continue to encode task-relevant information in absence of descending feedback. Indeed, their method circumvents the known limitations of more modern optogenetic or chemogenetic silencing, e.g. variable efficacy.

I also see three weaknesses which limit what we can learn from the authors' hard work, at least in the current form. I want to emphasize that these issues do not reflect any fatal flaw of the approach. Rather, I believe that their datasets likely contain the treasure-trove of knowledge required to completely support their claims.

(1) The conclusion of this paper requires the following assumption to be true: That the difference in neural activity between Hit and Miss trials reflects "information beyond the physical attributes of sound." The data presentation complicates asserting this assumption. Specifically, they average fluorescence transients of all Hit and all Miss trials in their detection task. Yet, Figure 3B shows that mice's d' depends on sound level, and since this is a detection task the smaller d' at low SPLs presumably reflects lower Hit rates (and thus higher Miss rates). As currently written, it is not clear if fluorescence traces for Hits arise from trials where the sound cue was played at a higher sound level than on Miss trials. Thus, the difference in neural activity on Hit and Miss trials could indeed reflect mice's behavior (licking or not licking). But in principle could also be explained by higher sound-evoked spike rates on Hit compared to Miss trials, simply due to louder click sounds. Indeed, the amplitude and decay tau of their indicator GCaMP6f is non-linearly dependent on the number and rate of spikes (Chen et al., 2013), so this isn't an unreasonable concern.

(2) The authors' central claim effectively rests upon two analyses in Figures 5 and 6. The spectral clustering algorithm of Figure 5 identifies 10 separate activity patterns in IC neurons of control and lesioned mice; most of these clusters show distinct activity on averaged Hit and Miss trials. They conclude that although the proportions of neurons from control and lesioned mice in certain clusters deviates from an expected 50/50 split, neurons from lesioned mice are still represented in all clusters. A significant issue here is that in addition to averaging all Hits and Miss trials together, the data from control and lesioned mice are lumped for the clustering. There is no direct comparison of neural activity between the two groups, so the reader must rely on interpreting a row of pie charts to assess the conclusion. It's unclear how similar task relevant activity is between control and lesioned mice; we don't even have a ballpark estimate of how auditory cortex does or does not contribute to task relevant activity. Although ideally the authors would have approached this by repeatedly imaging the same IC neurons before and after lesioning auditory cortex, this within-subjects design may be unfeasible if lesions interfere with task retention. Nevertheless, they have recordings from hundreds to thousands of neurons across two groups, so even a small effect should be observable in a between-groups comparison.

(3) In Figure 6, the authors show that logistic regression models predict whether the trial is a Hit or Miss from their fluorescence data. Classification accuracy peaks rapidly following sound presentation, implying substantial information regarding mice's actions. The authors further show that classification accuracy is reduced, but still above chance in mice with auditory cortical lesions. The authors conclude from this analysis task relevant activity persists in absence of auditory cortex. In principle I do not disagree with their conclusion.

The weakness here is in the details. First, the reduction in classification accuracy of lesioned mice suggests that auditory cortex does nevertheless transmit some task relevant information, however minor it may be. I feel that as written, their narrative does not adequately highlight this finding. Rather one could argue that their results suggest redundant sources of task-relevant activity converging in the IC. Secondly, the authors conclude that decoding accuracy is impaired more in partially compared to fully lesioned mice. They admit that this conclusion is at face value counterintuitive, and provide compelling mechanistic arguments in the Discussion. However, aside from shaded 95% CIs, we have no estimate of variance in decoding accuracy across sessions or subjects for either control or lesioned mice. Thus we don't know if the small sample sizes of partial (n = 3) and full lesion (n = 4) groups adequately sample from the underlying population. Their result of Figure 6B may reflect spurious sampling from tail ends of the distributions, rather than a true non-monotonic effect of lesion size on task relevant activity in IC.

Our responses to the ‘recommendations for the authors’ below lay out in detail how we addressed each comment and concern. Besides filling in key information about how our original analysis aimed at minimizing any potential impact of differences in sound level distributions - namely that trials used for decoding were limited to a subset of sound levels - and which was accidentally omitted in the original manuscript, we have now carried out several additional analyses.

We would like to highlight one of these because it supplements both the clustering and decoding analysis that we conducted to compare hit and miss trial activity, and directly addresses what the reviewer identified as our work’s main weakness (a possible confound between animal behavior and sound level distributions) and the request for an analysis that operates at the level of single units rather than the population level. Specifically, we assessed, separately for each recorded neuron, whether there was a statistically significant difference in the magnitude of neural activity between hit and miss trials. This approach allowed us to fully balance the numbers of hit and miss trials at each sound level that were entered into the analysis. The results revealed that a large proportion (close to 50%) of units were task modulated, i.e. had significantly different response magnitudes between hit and miss trials, and that this proportion was not significantly different between lesioned and non-lesioned mice. We hope that this, together with the rest of our responses, convincingly demonstrates that the shell of the IC encodes mouse sound detection behavior even when top-down input from the auditory cortex is absent.

Reviewer #2 (Public Review):

Summary:

This study takes a new approach to studying the role of corticofugal projections from auditory cortex to inferior colliculus. The authors performed two-photon imaging of cortico-recipient IC neurons during a click detection task in mice with and without lesions of auditory cortex. In both groups of animals, they observed similar task performance and relatively small differences in the encoding of task-response variables in the IC population. They conclude that non-cortical inputs to the IC provide can substantial task-related modulation, at least when AC is absent. Strengths:

This study provides valuable new insight into big and challenging questions around top-down modulation of activity in the IC. The approach here is novel and appears to have been executed thoughtfully. Thus, it should be of interest to the community.

Weaknesses: There are, however, substantial concerns about the interpretation of the findings and limitations to the current analysis. In particular, Analysis of single unit activity is absent, making interpretation of population clusters and decoding less interpretable. These concerns should be addressed to make sure that the results can be interpreted clearly in an active field that already contains a number of confusing and possibly contradictory findings.

Our responses to the ‘recommendations for the authors’ below lay out in detail how we addressed each comment and concern. Several additional analyses have now been carried out including ones that operate at the level of single units rather than the population level, as requested by the reviewer. We would like to briefly highlight one here because it supplements both the clustering and decoding analysis that we conducted to compare hit and miss trial activity and directly addresses what the other reviewers identified as our work’s main weakness (a possible confound between animal behavior and sound level distributions). Specifically, we assessed, separately for each recorded neuron, whether there was a statistically significant difference in the magnitude of neural activity between hit and miss trials. This approach allowed us to fully balance the numbers of hit and miss trials at each sound level that were entered into the analysis. The results revealed that a large proportion (close to 50%) of units were task modulated, i.e. had significantly different response magnitudes between hit and miss trials, and that this proportion was not significantly different between lesioned and non-lesioned mice. We hope that this, together with the rest of our responses, convincingly demonstrates that the shell of the IC encodes mouse sound detection behavior even when top-down input from the auditory cortex is absent.

Reviewer #3 (Public Review):

Summary:

This study aims to demonstrate that cortical feedback is not necessary to signal behavioral outcome to shell neurons of the inferior colliculus during a sound detection task. The demonstration is achieved by the observation of the activity of cortico-recipient neurons in animals which have received lesions of the auditory cortex. The experiment shows that neither behavior performance nor neuronal responses are significantly impacted by cortical lesions except for the case of partial lesions which seem to have a disruptive effect on behavioral outcome signaling. Strengths:

The experimental procedure is based on state of the art methods. There is an in depth discussion of the different effects of auditory cortical lesions on sound detection behavior. Weaknesses:

The analysis is not documented enough to be correctly evaluated. Have the authors pooled together trials with different sound levels for the key hit vs miss decoding/clustering analysis? If so, the conclusions are not well supported, as there are more misses for low sound levels, which would completely bias the outcome of the analysis. It would possible that the classification of hit versus misses actually only reflects a decoding of sound level based on sensory responses in the colliculus, and it would not be surprising then that in the presence or absence of cortical feedback, some neurons responds more to higher sound levels (hits) and less to lower sound levels (misses). It is important that the authors clarify and in any case perform an analysis in which the classification of hits vs misses is done only for the same sound levels. The description of feedback signals could be more detailed although it is difficult to achieve good temporal resolution with the calcium imaging technique necessary for targeting cortico-recipient neurons.

Our responses to the ‘recommendations for the authors’ below lay out in detail how we addressed each comment and concern. Besides filling in key information about how our original analysis aimed at minimizing any potential impact of differences in sound level distributions - namely that trials used for decoding were limited to a subset of sound levels - and which was accidentally omitted in the original manuscript, we have now carried out several additional analyses to directly address what the reviewer identified as our work’s main weakness (a possible confound between animal behavior and sound level distributions). This includes an analysis in which we were able to demonstrate for one imaging session with a sufficiently large number of trials that limiting the trials entered into the decoding analysis to those from a single sound level did not meaningfully impact decoding accuracy. We would like to highlight another new analysis here because it supplements both the clustering and decoding analyses that we conducted to compare hit and miss trial activity and addresses the other reviewers’ request for an analysis that operates at the level of single units rather than the population level. Specifically, we assessed, separately for each recorded neuron, whether there was a statistically significant difference in the magnitude of neural activity between hit and miss trials. This approach allowed us to fully balance the numbers of hit and miss trials at each sound level that were entered into the analysis. The results revealed that a large proportion (close to 50%) of units were task modulated, i.e. had significantly different response magnitudes between hit and miss trials, and that this proportion was not significantly different between lesioned and non-lesioned mice. We hope that this, together with the rest of our responses, convincingly demonstrates that the shell of the IC encodes mouse sound detection behavior even when top-down input from the auditory cortex is absent.

Reviewer #1 (Recommendations For The Authors):

Thank you for the opportunity to read your paper. I think the conclusion is exciting. Indeed, you indicate that perhaps contrary to many of our (untested) assumptions, task-relevant activity in the IC may persist in absence of auditory cortex.

As mentioned in my public review: Despite my interest in the work, I also think that there are several opportunities to significantly strengthen your conclusions. I feel this point is important because your work will likely guide the efforts of future students and post-docs working on this topic. The data can serve as a beacon to move the field away from the (somewhat naïve) idea that the evolved forebrain imparts behavioral relevance upon an otherwise uncivilized midbrain. This knowledge will inspire a search for alternative explanations. Indeed, although you don't highlight it in your narrative, your results dovetail nicely with several studies showing task-relevant activity in more ventral midbrain areas that project to the IC (e.g., pedunculopontine nuclei; see work from Hikosaka in monkeys, and more recently in mice from Karel Svoboda's lab).

Thanks for the kind words.

These studies, in particular the work by Inagaki et al. (2022) outlining how the transformation of an auditory go signal into movement could be mediated via a circuit involving the PPN/MRN (which might rely on the NLL for auditory input) and the motor thalamus, are indeed highly relevant.

We made the following changes to the manuscript text.

Line 472:”...or that the auditory midbrain, thalamus and cortex are bypassed entirely if simple acousticomotor transformations, such as licking a spout in response to a sound, are handled by circuits linking the auditory brainstem and motor thalamus via pedunculopontine and midbrain reticular nuclei (Inagaki et al., 2022).”

The beauty of the eLife experiment is that you are free to incorporate or ignore these suggestions. After all, it's your paper, not mine. Nevertheless, I hope you find my comments useful.<br /> First, a few suggestions to address my three comments in the public review.

Suggestion for public comment #1: An easy way to address this issue is to average the neural activity separately for each trial outcome at each sound level. That way you can measure if fluorescence amplitude (or integral) varies as a function of mice's action rather than sound level. This approach to data organization would also open the door to the additional analyses for addressing comment #2, such as directly comparing auditory and putatively non-auditory activity in neurons recorded from control and lesioned mice.

We have carried out additional analyses for distinguishing between the two alternative explanations of the data put forward by the reviewer: That the difference in neural activity between hit and miss trials reflects a) behavior or b) sound level (more precisely: differences in response magnitude arising from a higher proportion of high-sound-level trials in the hit trial group than in the miss trial group). If the data favored b), we would expect no difference in activity between hit and miss trials when plotted separately for each sound level. The new Figure 4 - figure supplement 1 indicates that this is not the case. Hit and miss trial activity are clearly distinct even when plotted separately for different sound levels, confirming that this difference in activity reflects the animals’ behavior rather than sensory information.

Changes to manuscript.

Line 214: “While averaging across all neurons cannot capture the diversity of responses, the averaged response profiles suggest that it is mostly trial outcome rather than the acoustic stimulus and neuronal sensitivity to sound level that shapes those responses (Figure 4 – figure supplement 1).”

Additionally, we assessed for each neuron separately whether there was a significant difference between hit and miss trial activity and therefore whether the activity of the neuron could be considered “task-modulated”. To achieve this, we used equal numbers of hit and miss trials at each sound level to ensure balanced sound level distributions and thus rule out any potential confound between sound level distributions and trial outcome. This analysis revealed that the proportion of task-modulated neurons was very high (close to 50%) and not significantly different between lesioned and non-lesioned mice (Figure 6 - figure supplement 3).

Changes to the manuscript.

Line 217: “Indeed, close to half (1272 / 2649) of all neurons showed a statistically significant difference in response magnitude between hit and miss trials…”

Line 307: “Although the proportion of individual neurons with distinct response magnitudes in hit and miss trials in lesioned mice did not differ from that in non-lesioned mice, it was significantly lower when separating out mice with partial lesions (Figure 6 – figure supplement 3).”

Differences in the distributions of sound levels in the different trial types could also potentially confound the decoding into hit and miss trials. Our original analysis was actually designed to take this into account but, unfortunately, we failed to include sufficient details in the methods section.

Changes to the manuscript.

Line 710: “Rather than including all the trials in a given session, only trials of intermediate difficulty were used for the decoding analysis. More specifically, we only included trials across five sound levels, comprising the lowest sound level that exceeded a d’ of 1.5 plus the two sound levels below and above that level. That ensured that differences in sound level distributions would be small, while still giving us a sufficient number of trials to perform the decoding analysis.“

In this context, it is worth bearing in mind that a) the decoding analysis was done on a frame-byframe basis, meaning that the decoding score achieved early in the trial has no impact on the decoding score at later time points in the trial, b) sound-driven activity predominantly occurs immediately after stimulus onset and is largely over about 1 s into the trial (see cluster 3, for instance, or average miss trial activity in Figure 4 – figure supplement 1), c) decoding performance of the behavioral outcome starts to plateau 500-1000 ms into the trial and remains high until it very gradually begins to decline after about 2 s into the trial. In other words, decoding performance remains high far longer than the stimulus would be expected to have an impact on the neurons’ activity. Therefore, we would expect any residual bias due to differences in the sound level distribution that our approach did not control for to be restricted to the very beginning of the trial and not to meaningfully impact the conclusions derived from the decoding analysis.

Finally, we carried out an additional decoding analysis for one imaging session in which we had a sufficient number of trials to perform the analysis not only over the five (59, 62, 65, 68, 71 dB SPL) original sound levels, but also over a reduced range of three (62, 65, 68 dB SPL) sound levels, as well as a single (65 dB SPL) sound level (Figure 6 - figure supplement 1). The mean sound level differences between the hit trial distributions and miss trial distributions for these three conditions were 3.08, 1.01 and 0 dB, respectively. This analysis suggests that decoding performance is not meaningfully impacted by changing the range of sound levels (and sound level distributions), other than that including fewer sound levels means fewer trials and thus noisier decoding.

Changes to manuscript.

Line 287: ”...and was not meaningfully affected by differences in sound level distributions between hit and miss trials (Figure 6 – figure supplement 1).”

Suggestion for public comment #2: Perhaps a solution would be to display example neuron activity in each cluster, recorded in control and lesioned mice. The reader could then visually compare example data from the two groups, and immediately grasp the conclusion that task relevant activity remains in absence of auditory cortex. Additionally, one possibility might be to calculate the difference in neural activity between Hit and Miss trials for each task-modulated neuron. Then, you could compare these values for neurons recorded in control and lesion mice. I feel like this information would greatly add to our understanding of cortico-collicular processing.

I would also argue that it's perhaps more informative to show one (or a few) example recordings rather than averaging across all cells in a cluster. Example cells would give the reader a better handle on the quality of the imaging, and this approach is more standard in the field. Finally, it would be useful to show the y axis calibration for each example trace (e.g. Figure 5 supp 1). That is also pretty standard so we can immediately grasp the magnitude of the recorded signal.

We agree that while the information we provided shows that neurons from lesioned and nonlesioned groups are roughly equally represented across the clusters, it does not allow the reader to appreciate how similar the activity profiles of neurons are from each of the two groups. However, picking examples can be highly subjective and thus potentially open to bias. We therefore opted instead to display, separately for lesioned and non-lesioned mice, the peristimulus time histograms of all neurons in each cluster, as well as the cluster averages of the response profiles (Figure 5 - figure supplement 3). This, we believe, convincingly illustrates the close correspondence between neural activity in lesioned and non-lesioned mice across different clusters. All our existing and new figures indicate the response magnitude either on the figures’ y-axis or via scale/color bars.

Changes to manuscript.

Line 254: “Furthermore, there was a close correspondence between the cluster averages of lesioned and non-lesioned mice (Figure 5 – figure supplement 3).”

Furthermore, we’ve now included a video of the imaging data which, we believe, gives the reader a much better handle on the data quality than further example response profiles would.

Changes to manuscript.

Line 197: ”...using two-photon microscopy (Figure 4B, Video 1).”

Suggestion for public comment #3: In absence of laborious and costly follow-up experiments to boost the sample size of partial and complete lesion groups, it may be more prudent to simply tone down the claims that lesion size differentially impacts decoding accuracy. The results of this analysis are not necessary for your main claims.

Our new results on the proportions of ‘task-modulated’ neurons (Figure 6 - figure supplement 3) across different experimental groups show that there is no difference between non-lesioned and lesioned mice as a whole, but mice with partial lesions have a smaller proportion of taskmodulated neurons than the other two groups. While this corroborates the results of the decoding analysis, we certainly agree that the small sample size is a caveat that needs to be acknowledged.

Changes to manuscript.

Line 477: ”Some differences were observed for mice with only partial lesions of the auditory cortex.

Those mice had a lower proportion of neurons with distinct response magnitudes in hit and miss trials than mice with (near-)complete lesions. Furthermore, trial outcomes could be read out with lower accuracy from these mice. While this finding is somewhat counterintuitive and is based on only three mice with partial lesions, it has been observed before that smaller lesions…”

A few more suggestions unrelated to public review:

Figure 1: This is somewhat of an oddball in this manuscript, and its inclusion is not necessary for the main point. Indeed, the major conclusion of Fig 1 is that acute silencing of auditory cortex impairs task performance, and thus optogenetic methods are not suitable to test your hypothesis. However, this conclusion is also easily supported from decades of prior work, and thus citations might suffice.

We do not agree that these data can easily be substituted with citations of prior published work. While previous studies (Talwar et al., 2001, Li et al., 2017) have demonstrated the impact of acute pharmacological silencing on sound detection in rodents, pharmacological and optogenetic silencing are not equivalent. Furthermore, we are aware of only one published study (Kato et al., 2015) that investigated the impact of optogenetically perturbing auditory cortex on sound detection (others have investigated its impact on discrimination tasks). Kato et al. (2015) examined the effect of acute optogenetic silencing of auditory cortex on the ability of mice to detect the offsets of very long (5-9 seconds) sounds, which is not easily comparable to the click detection task employed by us. Furthermore, when presenting our work at a recent meeting and leaving out the optogenetics results due to time constraints, audience members immediately enquired whether we had tried an optogenetic manipulation instead of lesions. Therefore, we believe that these data represent a valuable piece of information that will be appreciated by many readers and have decided not to remove them from the manuscript.

A worst case scenario is that Figure 1 will detract from the reader's assessment of experimental rigor. The data of 1C are pooled from multiple sessions in three mice. It is not clear if the signed-rank test compares performance across n = 3 mice or n = 13 sessions. If the latter, a stats nitpicker could argue that the significance might not hold up with a nested analysis considering that some datapoints are not independent of one another. Finally, the experiment does not include a control group, gad2-cre mice injected with a EYFP virus. So as presented, the data are equally compatible with the pessimistic conclusion that shining light into the brain impairs mice's licking. My suggestion is to simply remove Figure 1 from the paper. Starting off with Figure 3 would be stronger, as the rest of the study hinges upon the knowledge that control and lesion mice's behavior is similar.

Instead of reporting the results session-wise and doing stats on the d’ values, we now report results per mouse and perform stats on the proportions of hits and false alarms separately for each mouse. The results are statistically significant for each mouse and suggest that the differences in d’ are primarily caused by higher false alarm rates during the optogenetic perturbation than in the control condition.

Changes to manuscript.

New Figure 1.

We agree that including control mice not expressing ChR2 would be important for fully characterizing the optogenetic manipulation and that the lack of this control group should be acknowledged. However, in the context of this study, the outcome of performing this additional experiment would be inconsequential. We originally considered using an optogenetic approach to explore the contribution of cortical activity to IC responses, but found that this altered the animals’ sound detection behavior. Whether that change in behavior is due to activation of the opsin or simply due to light being shone on the brain has no bearing on the conclusion that this type of manipulation is unsuitable for determining whether auditory cortex is required for the choice-related activity that we recorded in the IC.

Changes to manuscript.

Line 106: ”Although a control group in which the auditory cortex was injected with an EYFP virus lacking ChR2 would be required to confirm that the altered behavior results from an opsindependent perturbation of cortical activity, this result shows that this manipulation is also unsuitable… ”

Figure 2, comment #1: The micrograph of panel B shows the densest fluorescence in the central IC. You interpret this as evidence of retrograde labeling of central IC neurons that project to the shell IC. This is a nice finding, but perhaps a more relevant micrograph would be to show the actual injection site in the shell layers. The rest of Figure 2 documents the non-auditory cortical sources of forebrain feedback. Since non-auditory cortical neurons may or may not target distinct shell IC sub-circuits, it's important to know where the retrograde virus was injected. Stylistic comment: The flow of the panels is somewhat unorthodox. Panel A and B follow horizontally, then C and D follow vertically, followed by E-H in a separate column. Consider sequencing either horizontally or vertically to maximize the reader's experience.

Figure 2, comment # 2: It would also be useful to show more rostral sections from these mice, perhaps as a figure supplement, if you have the data. I think there is a lot of value here given a recent paper (Olthof et al., 2019 Jneuro) arguing that the IC receives corticofugal input from areas more rostral to the auditory cortex. So it would be beneficial for the field to know if these other cortical sources do or do not represent likely candidates for behavioral modulation in absence of auditory cortex.

Figure 2, comment #3: You have a striking cluster of retrogradely labeled PPC neurons, and I'm not sure PPC has been consistently reported as targeting the IC. It would be good to confirm that this is a "true" IC projection as opposed to viral leakage into the SC. Indeed, Figure 2, supplement 2 also shows some visual cortex neurons that are retrogradely labeled. This has bearing on the interpretations, because choice-related activity is rampant in PPC, and thus could be a potential source of the task relevant activity that persists in your recordings. This could be addressed as the point above, by showing the SC sections from these same mice.

All IC injections were made under visual guidance with the surface of the IC and adjacent brain areas fully exposed after removal of the imaging window. Targeting the IC and steering clear of surrounding structures, including the SC, was therefore relatively straightforward.

We typically observed strong retrograde labeling in the central nucleus after viral injections into the dorsal IC and, given the moderate injection volume (~50 nL at each of up to three sites), it was also typical to see spatially fairly confined labeling at the injection sites. For the mouse shown in Figure 2, we do not have further images of the IC. This was one of the earliest mice to be included in the study and we did not have access to an automatic slide scanner at the time. We had to acquire confocal images in a ‘manual’ and very time-consuming manner and therefore did not take further IC images for this mouse. We have now included, however, a set of images spanning the whole IC and the adjacent SC sections for the mouse for which we already show sections in Figure 2 - figure supplement 2. These were added as Figure 2 - figure supplement 3A to the manuscript. These images show that the injections were located in the caudal half of the IC and that there was no spillover into the SC - close inspection of those sections did not reveal any labeled cell bodies in the SC. Furthermore, we include as Figure 2 - figure supplement 3B a dozen additional rostral cortical sections of the same mouse illustrating corticocollicular neurons in regions spanning visual, parietal, somatosensory and motor cortex. Given the inclusion of the IC micrographs in the new supplementary figure, we removed panel B from Figure 2. This should also make it easier for the reader to follow the sequencing of the remaining panels.

Changes to manuscript.

New Figure 2 - figure supplement 3.

Line 159: “After the experiments, we injected a retrogradely-transported viral tracer (rAAV2-retrotdTomato) into the right IC to determine whether any corticocollicular neurons remained after the auditory cortex lesions (Figure 2, Figure 2 – figure supplement 2, Figure 2 – figure supplement 3). The presence of retrogradely-labeled corticocollicular neurons in non-temporal cortical areas (Figure 2) was not the result of viral leakage from the dorsal IC injection sites into the superior colliculus (Figure 2 – figure supplement 3).”

Line 495: “...projections to the IC, such as those originating from somatosensory cortical areas (Lohse et al., 2021; Lesicko et al., 2016) and parietal cortex may have contributed to the response profiles that we observed.

Figure 5 (see also public review point #2): I am not convinced that this unsupervised method yields particularly meaningful clusters; a grain of salt should be provided to the reader. For example, Clusters 2, 5, 6, and 7 contain neurons that pretty clearly respond with either short latency excitation or inhibition following the click sound on Hits. I would argue that neurons with such diametrically opposite responses should not be "classified" together. You can see the same issue in some of Namboodiri/Stuber's clustering (their Figure 1). It might be useful to make it clear to the reader that these clusters can reflect idiosyncrasies of the algorithm, the behavior task structure, or both.

We agree.

Changes to manuscript.

Line 666: “While clustering is a useful approach for organizing and visualizing the activity of large and heterogeneous populations of neurons, we need to be mindful that, given continuous distributions of response properties, the locations of cluster boundaries can be somewhat arbitrary and/or reflect idiosyncrasies of the chosen method and thus vary from one algorithm to another. We employed an approach very similar to that described in Namboodiri et al. (2019) because it is thought to produce stable results in high-dimensional neural data (Hirokawa et al. 2019).”

Methods:

How was a "false alarm" defined? Is it any lick happening during the entire catch trial, or only during the time period corresponding to the response window on stimulus trials?

The response window was identical for catch and stimulus trials and a false alarm was defined as licking during the response window of a catch trial.

Changes to manuscript.

Line 598: “During catch trials, neither licking (‘false alarm’) during the 1.5-second response window …”

L597 and so forth: What's the denominator in the conversion from the raw fluorescence traces into DF/F? Did you take the median or mode fluorescence across a chunk of time? Baseline subtract average fluorescence prior to click onset? Similarly, please provide some more clarification as to how neuropil subtraction was achieved. This information will help us understand how the classifier can decode trial outcome from data prior to sound onset.

Signal processing did not involve the subtraction of a pre-stimulus period.

Changes to manuscript.

Line 629: ”Neuropil extraction was performed using default suite2p parameters (https://suite2p.readthedocs.io/en/latest/settings.html), neuropil correction was done using a coefficient of 0.7, and calcium ΔF/F signals were obtained by using the median over the entire fluorescence trace as F0. To remove slow fluctuations in the signal, a baseline of each neuron’s entire trace was calculated by Gaussian filtering in addition to minimum and maximum filtering using default suite2p parameters. This baseline was then subtracted from the signal.”

Was the experimenter blinded to the treatment group during the behavior experiments? If not, were there issues that precluded blinding (limited staffing owing to lab capacity restrictions during the pandemic)? This is important to clarify for the sake of rigor and reproducibility.

Changes to manuscript.

Line 574: “The experimenters were not blinded to the treatment group, i.e. lesioned or non-lesioned, but they were blind to the lesion size both during the behavior experiments and most of the data processing.”

Minor:

L127-128: "In order to test...lesioned the auditory cortex bilaterally in 7 out of 16 animals". I would clarify this by changing the word animals to "mice" and 7 out of 16 by stating n = 9 and n = 7 are control and lesion groups, respectively.

Agreed.

Changes to manuscript.

Line 129: “...compared the performance of mice with bilateral lesions of the auditory cortex (n = 7) with non-lesioned controls (n = 9)”

L225-226: You rule out self-generated sounds as a likely source of behavioral modulation by citing Nate Sawtell's paper in the DCN. However, Stephen David's lab suggested that in marmosets, post sound activity in central IC may in fact reflect self-generated sounds during licking. I suggest addressing this with a nod to SVD's work (Singla et al., 2017; but see Shaheen et al., 2021).

Agreed.

Changes to manuscript.

Line 243: “(Singla et al., 2017; but see Shaheen et al., 2021)”

Line 238 - 239: You state that proportions only deviate greater than 10% for one of the four statistically significant clusters. Something must be unclear here because I don't understand: The delta between the groups in the significant clusters of Fig 5C is (from left to right) 20%, 20%, 38%, and 12%. Please clarify.

Our wording was meant to convey that a deviation “from a 50/50 split” of 10% means that each side deviates from 50 by 10% resulting in a 40/60 (or 60/40) split. We agree that that has the potential to confuse readers and is not as clear as it could be and have therefore dropped the ambiguous wording.

Changes to manuscript.

Line 253: ”,..the difference between the groups was greater than 20% for only one of them.”

L445: I looked at the cited Allen experiment; I'd be cautious with the interpretation here. A monosynaptic IC->striatum projection is news to me. I think Allen Institute used an AAV1-EGFP virus for these experiments, no? As you know, AAV1 is quite transsynaptic. The labeled fibers in striatum of that experiment may reflect disynaptic labeling of MGB neurons (which do project to striatum).

Agreed. We deleted the reference to this Allen experiment.

L650: Please define "network activity". Is this the fluorescence value for each ROI on each frame of each trial? Averaged fluorescence of each ROI per frame? Total frame fluorescence including neuropil? Depending on who you ask, each of these measures provides some meaningful readout of network activity, so clarification would be useful.

Changes to manuscript.

Line 707: “Logistic regression models were trained on the network activity of each session, i.e., the ΔF/F values of all ROIs in each session, to classify hit vs miss trials. This was done on a frame-by-frame basis, meaning that each time point (frame) of each session was trained separately.

Figure 3 narrative or legend: Listing the F values for the anova would be useful. There is pretty clearly a main effect of training session for hits, but what about for the false alarms? That information is important to solidify the result, and would help more specialized readers interpret the d-prime plot in this figure.

Agreed. There were significant main effects of training day for both hit rates and false alarm rates (as well as d’).

Changes to manuscript.

Line 165: “The ability of the mice to learn and perform the click detection task was evident in increasing hit rates and decreasing false alarm rates across training days (Figure 3A, p < 0.01, mixed-design ANOVAs).”

In summary, thank you for undertaking this work. Your conclusions are provocative, and thus will likely influence the field's direction for years to come.

Thank you for those kind words and valuable and constructive feedback, which has certainly improved the manuscript.

Reviewer #2 (Recommendations For The Authors):

MAJOR CONCERNS

(1) (Fig. 5) What fraction of individual neurons actually encode task-related information in each animal group? How many neurons respond to sound? The clustering and decoding analyses are interesting, but they obscure these simple questions, which get more directly at the main questions of the study. Suggested approach: For a direct comparison of AC-lesioned and -non-lesioned animals, why not simply compare the mean difference between PSTH response for each neuron individually? To test for trial outcome effects, compare Hit and Miss trials (same stimulus, different behavior) and for sound response effects, compare Hit and False alarm trials (same behavior, different response). How do you align for time in the latter case when there's no stimulus? Align to the first lick event. The authors should include this analysis or explain why their approach of jumping right to analysis of clusters is justified.

We have now calculated the fraction of neurons that encode trial outcome by comparing hit and miss trial activity. That fraction does not differ between non-lesioned animals and lesioned animals as a whole, but is significantly smaller in mice with partial lesions. The author’s suggestion of comparing hit and false alarm trial activity to assess sound responsiveness is problematic because hit trials involve reward delivery and consumption. Consequently, they are behaviorally very different from false alarm trials (not least because hit trials tend to contain much more licking). Therefore, we calculated the fraction of neurons that respond to the acoustic stimulus by comparing activity before and after stimulus onset in miss trials. We found no significant difference between the non-lesioned and lesioned mice or between subgroups.

We have addressed these points with the following changes to the manuscript:

Line 217: “Indeed, close to half (1272 / 2649) of all neurons showed a statistically significant difference in response magnitude between hit and miss trials, while only a small fraction (97 / 2649) exhibited a significant response to the sound.”

Line 307: “Although the proportion of individual neurons with distinct response magnitudes in hit and miss trials in lesioned mice did not differ from that in non-lesioned mice, it was significantly lower when separating out mice with partial lesions (Figure 6 – figure supplement 3).”

Line 648: “Analysis of task-modulated and sound-driven neurons. To identify individual neurons that produced significantly different response magnitudes in hit and miss trials, we calculated the mean activity for each stimulus trial by taking the mean activity over the 5 seconds following stimulus presentation and subtracting the mean activity over the 2 seconds preceding the stimulus during that same trial. A Mann-Whitney U test was then performed to assess whether a neuron showed a statistically significant difference (Benjamini-Hochberg adjusted p-value of 0.05) in response magnitude between hit and miss trials. The analysis was performed using equal numbers of hit and miss trials at each sound level to ensure balanced sound level distributions. If, for a given sound level, there were more hit than miss trials, we randomly selected a sample of hit trials (without substitution) to match the sample size for the miss trials and vice versa. Sounddriven neurons were identified by comparing the mean miss trial activity before and after stimulus presentation. Specifically, we performed a Mann-Whitney U test to assess whether there was a statistically significant difference (Benjamini-Hochberg adjusted p-value of 0.05) between the mean activity over the 2 seconds preceding the stimulus and the mean activity over the 1 second period following stimulus presentation.”

Some more specific concerns about focusing only on cluster-level and population decoding analysis are included below.

(2) (L 234) "larger field of view". Do task-related or lesion-dependent effects depend on the subregion of IC imaged? Some anatomists would argue that the IC shell is not a uniform structure, and concomitantly, task-related effects may differ between fields. Did coverage of IC subregions differ between experimental groups? Is there any difference in task related effects between subregions of IC? Or maybe all this work was carried out only in the dorsal area? The differences between lesioned and non-lesioned animals are relatively small, so this may not have a huge impact, but a more nuanced discussion that accounts for observed or potential (if not tested) differences between regions of the IC.

The specific subregion coverage could also impact the decoding analysis (Fig 6), and if possible it might be worth considering an interaction between field of view and lesion size on decoding.

Each day we chose a new imaging location to avoid recording the same neurons more than once and aimed to sample widely across the optically accessible surface of the IC. We typically stopped the experiment only when there were no more new areas to record from. In terms of the depth of the imaged neurons, we were limited by the fact that corticorecipient neurons become sparser with depth and that the signal available from the GCaMP6f labeling of the Ai95 mice becomes rapidly weaker with increasing distance from the surface. This meant that we recorded no deeper than 150 µm from the surface of the IC. Consequently, while there may have been some variability in the average rostrocaudal and mediolateral positioning of imaging locations from animal to animal due to differences between mice in how much of the IC surface was visible, cranial window positioning, and in neuronal labeling etc, our dataset is anatomically uniform in that all recorded neurons receive input from the auditory cortex and are located within 150 µm of the surface of the IC. Therefore, we think it highly unlikely that small sampling differences across animals could have a meaningful impact on the results.

Given that there is no consensus as to where the border between the dorsal and external/lateral cortices of the IC is located and that it is typically difficult to find reliable anatomical reference points (the location of the borders between the IC and surrounding structures is not always obvious during imaging, i.e. a transition from a labeled area to a dark area near the edge of the cranial window could indicate a border with another structure, but also the IC surface sloping away from the window or simply an unlabeled area within the IC), we made no attempt to assign our recordings from corticorecipient neurons to specific subdivisions of the IC.

Changes to manuscript.

Line 195: “We then proceeded to record the activity of corticorecipient neurons within about 150 µm of the dorsal surface of the IC using two-photon microscopy (Figure 4B, Video 1).”

Line 375: “We imaged across the optically accessible dorsal surface of the IC down to a depth of about 150 µm below the surface. Consequently, the neurons we recorded were located predominantly in the dorsal cortex. However, identifying the borders between different subdivisions of the IC is not straightforward and we cannot rule out the possibility that some were located in the lateral cortex.”

(3) (L 482-483) "auditory cortex is not required for the task-related activity recording in IC neurons of mice performing a sound detection task". Most places in the text are clearer, but this statement is confusing. Yes, animals with lesions can have a "normal"-looking IC, but does that mean that AC does not strongly modulate IC during this behavior in normal animals? The authors have shown convincingly that subcortical areas can both shape behavior and modulate IC normally, but AC may still be required for IC modulation in non-lesioned animals. Given the complexity of this system, the authors should make sure they summarize their results consistently and clearly throughout the manuscript.

The reviewer raises an important point. What we have shown is that corticorecipient dorsal IC neurons in mice without auditory cortex show neural activity during a sound detection task that is largely indistinguishable from the activity of mice with an intact auditory cortex. In lesioned mice, the auditory cortex is thus not required. Whether the IC activity of the non-lesioned group can be shaped by input from the auditory cortex in a meaningful way in other contexts, such as during learning, is a question that our data cannot answer.

Changes to manuscript.

Line 508: "While modulation of IC activity by this descending projection has been implicated in various functions, most notably in the plasticity of auditory processing, we have shown in mice performing a sound detection task that IC neurons show task-related activity in the absence of auditory cortical input."

LESSER CONCERNS

(L. 106-107) "Optogenetic suppression of cortical activity is thus also unsuitable..." It appears that behavior is not completely abolished by the suppression. One could also imagine using a lower dose of muscimol for partial inactivation of AC feedback. When some behavior persists, it does seem possible to measure task-related changes in the IC. This may not be necessary for the current study, but the authors should consider how these transient methods could be applied usefully in the Discussion. What about inactivation of cortical terminals in the IC? Is that feasible?

Our argument is not that acute manipulations are unsuitable because they completely abolish the behavior, but because they significantly alter the behavior. Although it would not be trivial to precisely measure the extent of pharmacological cortical silencing in behaving mice that have been fitted with a midbrain window, it should be possible to titrate the size of a muscimol injection to achieve partial silencing of the auditory cortex that does not fully abolish the ability to detect sounds. However, such an outcome would likely render the data uninterpretable. If no effect on IC activity was observed, it would not be possible to conclude whether this was due to the fact that the auditory cortex was only partially silenced or that projections from the auditory cortex have no influence on the recorded IC activity. Similarly, if IC activity was altered, it would not be possible to say whether this was due to altered descending modulation resulting from the (partially) silenced auditory cortex or to the change in behavior, which would likely be reflected in the choice-related activity measured in the IC.

Silencing of corticocollicular axons in the IC is potentially a more promising approach and we did devote a considerable amount of time and effort to establishing a method that would allow us to simultaneously image IC neurons while silencing corticocollicular axons, trying both eNpHR3.0 and Jaws with different viral labeling approaches and mouse lines. However, we ultimately abandoned those attempts because we were not convinced that we had achieved sufficient silencing or that we would be able to convincingly verify this. Furthermore, axonal silencing comes with its own pitfalls and the interpretation of its consequences is not straightforward. Given that our discussion already contains a section (line 421) on axonal silencing, we do not feel there would be any benefit in adding to that.

(Figure 1). Can the authors break down the performance for FA and HR, as they do in Fig. 3? It would be helpful to know what aspect of behavior is impaired by the transient inactivation.

Good point. Figure 1 has been updated to show the results separately for hit rates, false alarms and d’. The new figure indicates that the change in d’ is primarily a consequence of altered false alarm rates. Please also see our response to a related comment by reviewer #1.

Changes to manuscript.

New figure 1.

(Figure 4 legend). Minor: Please clarify, what is time 0 in panel C? Time of click presentation?

Yes, that is correct.

Changes to manuscript.

Line 209: ”Vertical line at time 0 s indicates time of click presentation.”

(L. 228-229). There has been a report of lick and other motor related activity in the IC - e.g., see Shaheen, Slee et al. (J Neurosci 2021), the timing of which suggests that some of it may be acoustically driven.

Thanks for pointing this out. Shaheen et al., 2021 should certainly have been cited by us in this context as well as in other parts of the manuscript.

Changes to manuscript.

Line 243: “(Singla et al., 2017; but see Shaheen et al., 2021)”

Also, have the authors considered measuring a peri-lick response? The difference between hit and miss trials could be perceptual or it could reflect differences in motor activity. This may be hard to tease apart, but, for example, one can test whether activity is stronger on trials with many licks vs. few licks?

(L. 261) "Behavior can be decoded..." similar or alternative to the previous question of evoked activity, can you decode lick events from the population activity?

The difference between hit and miss trial activity almost certainly partially reflects motor activity associated with licking. This was stated in the Discussion, but to make that point more explicitly, we now include a plot of average false alarm trial activity, i.e. trials without sound (catch trials) in which animals licked (but did not receive a reward).

Given a sufficient number of catch trials, it should be possible to decode false alarm and correct rejection trials. However, our experiment was not designed with that in mind and contains a much smaller number of catch trials than stimulus trials (approximately one tenth the number of stimulus trials), so we have not attempted this.

Changes to manuscript.

New Figure 4 - figure supplement 1.

(L. 315) "Pre-stimulus activity..." Given reports of changes in activity related to pupil-indexed arousal in the auditory system, do the authors by any chance have information about pupil size in these datasets?

Given that all recordings were performed in the dark, fluctuations in pupil diameter were relatively small. Therefore, we have not made any attempt to relate pupil diameter to any of the variables assessed in this manuscript.

(L. 412) "abolishes sound detection". While not exactly the same task, the authors might comment on Gimenez et al (J Neurophys 2015) which argued that temporary or permanent lesioning of AC did not impair tone discrimination. More generally, there seems to be some disagreement about what effects AC lesions have on auditory behavior.

Thank you for this suggestion. Gimenez et al. (2015) investigated the ability of freely moving rats to discriminate sounds (and, in addition, how they adapt to changes in the discrimination boundary). Broadly consistent with later reports by Ceballo et al. (2019) (mild impairment) and O’Sullivan et al. (2019) (no impairment), Gimenez et al. (2015) reported that discrimination performance is mildly impaired after lesioning auditory cortex. Where the results of Gimenez et al. (2015) stand out is in the comparatively mild impairments that were seen in their task when they used muscimol injections, which contrast with the (much) larger impairments reported by others (e.g. Talwar et al., 2001; Li et al., 2017; Jaramillo and Zador, 2014).

Changes to manuscript.

Line 433: ”However, transient pharmacological silencing of the auditory cortex in freely moving rats (Talwar et al., 2001), as well as head-fixed mice (Li et al., 2017), completely abolishes sound detection (but see Gimenez et al., 2015).”

(L. 649) "... were generally separable" Is the claim here that the clusters are really distinct from each other? This is unexpected, and it might be helpful if the authors could show this result in a figure.

The half-sentence that this comment refers to has been removed from the methods section. Please also see a related comment by reviewer #1 which prompted us to add the following to the methods section.

Changes to manuscript.

Line 666: “While clustering is a useful approach for organizing and visualizing the activity of large and heterogeneous populations of neurons we need to be mindful that, given continuous distributions of response properties, the locations of cluster boundaries can be somewhat arbitrary and/or reflect idiosyncrasies of the chosen method and thus vary from one algorithm to another. We employed an approach very similar to that described in Namboodiri et al. (2019) because it is thought to produce stable results in high-dimensional neural data (Hirokawa et al. 2019).”

Reviewer #3 (Recommendations For The Authors):

(1) The authors must absolutely clarify if the hit versus misses decoding and clustering analysis is done for a single sound level or for multiple sound levels (what is the fraction of trials for each sound leve?). If the authors did it for multiple sound levels they should redo all analyses sound-level by sound-level, or for a single sound level if there is one that dominates. No doubt that there is information about the trial outcome in IC, but it should not be over-estimated by a confound with stimulus information.

This is an important point. The original clustering analysis was carried out across different sound levels. We have now carried out additional analysis for distinguishing between two alternative explanations of the data, which were also raised by reviewer #1. – that the difference in neural activity between hit and miss trials could reflect a) the animals’ behavior or b) relatively more hit trials at higher sound levels, which would be expected to produce stronger responses. If the data favored b), we would expect no difference in activity between hit and miss trials when plotted separately for different sound levels. The new figure 4 - figure supplement 1 indicates that that is not the case. Hit and miss trial activity are clearly distinct even when plotted separately for different sound levels, confirming that this difference in activity reflects the animals’ behavior rather than sensory information.

We made the following changes to manuscript.

Line 214: “While averaging across all neurons cannot capture the diversity of responses, the averaged response profiles suggest that it is mostly trial outcome rather than the acoustic stimulus and neuronal sensitivity to sound level that shapes those responses (Figure 4 – figure supplement 1).”

Differences in the distributions of sound levels in the different trial types could also potentially confound the decoding into hit and miss trials. Our analysis actually aimed to take this into account but, unfortunately, we failed to include sufficient details in the methods section.

Changes to manuscript.

Line 710: “Rather than including all the trials in a given session, only trials of intermediate difficulty were used for the decoding analysis. More specifically, we only included trials across five sound levels, comprising the lowest sound level that exceeded a d’ of 1.5 plus the two sound levels below and above that level. That ensured that differences in sound level distributions would be small, while still giving us a sufficient number of trials to perform the decoding analysis.“

In this context, it is worth bearing in mind that a) the decoding analysis was done on a frame-byframe basis, meaning that the decoding score achieved early in the trial has no impact on the decoding score at later time points in the trial, b) sound-driven activity predominantly occurs immediately after stimulus onset and is largely over about 1 s into the trial (see cluster 3, for instance, or average miss trial activity in figure 4 - figure supplement 1), c) decoding performance of the behavioral outcome starts to plateau 500-1000 ms into the trial and remains high until it very gradually begins to decline after about 2 s into the trial. In other words, decoding performance remains high far longer than the stimulus would be expected to have an impact on the neurons’ activity. Therefore, we would expect any residual bias due to differences in the sound level distribution that our approach did not control for to be restricted to the very beginning of the trial and not to meaningfully impact the conclusions derived from the decoding analysis.

Furthermore, we carried out an additional decoding analysis for one imaging session in which we had a sufficient number of trials to perform the analysis not only over the five (59, 62, 65, 68, 71 dB SPL) original sound levels, but also over a reduced range of three (62, 65, 68 dB SPL) sound levels, as well as a single (65 dB SPL) sound level (Figure 6 - figure supplement 1). The mean sound level difference between the hit trial distributions and miss trial distributions for these three conditions were 3.08, 1.01 and 0 dB, respectively. This analysis suggests that decoding performance is not meaningfully impacted by changing the range of sound levels (and sound level distributions) other than that including fewer sound levels means fewer trials and thus noisier decoding.

Changes to manuscript.

Line 287: ”...and was not meaningfully affected by differences in sound level distributions between hit and miss trials (Figure 6 – figure supplement 1).”

Finally, in order to supplement the decoding analysis, we determined for each individual neuron whether there was a significant difference between the average hit and average miss trial activity. Note that this was done using equal numbers of hit and miss trials at each sound level to ensure balanced sound level distributions and to rule out any potential confound of sound level. This revealed that the proportion of neurons containing “information about trial outcome” was generally very high, close to 50% on average, and not significantly different between lesioned and non-lesioned mice.

Changes to manuscript.

Line 307: “Although the proportion of individual neurons with distinct response magnitudes in hit and miss trials in lesioned mice did not differ from that in non-lesioned mice, it was significantly lower when separating out mice with partial lesions (Figure 6 – figure supplement 3).”

Line 648: “Analysis of task-modulated and sound-driven neurons. To identify individual neurons that produced significantly different response magnitudes in hit and miss trials, we calculated the mean activity for each stimulus trial by taking the mean activity over the 5 seconds following stimulus presentation and subtracting the mean activity over the 2 seconds preceding the stimulus during that same trial. A Mann-Whitney U test was then performed to assess whether a neuron showed a statistically significant difference (Benjamini-Hochberg adjusted p-value of 0.05) in response magnitude between hit and miss trials. The analysis was performed using equal numbers of hit and miss trials at each sound level to ensure balanced sound level distributions. If, for a given sound level, there were more hit than miss trials we randomly selected a sample of hit trials (without substitution) to match the sample size for the miss trials and vice versa. ”

(2) I have the feeling that the authors do not exploit fully the functional data recorded with two-imaging. They identify several cluster but do not describe their functional differences. For example, cluster 3 is obviously mainly sensory driven as it is not modulated by outcome. This could be mentioned. This could also be used to rule out that trial outcome is the results of insufficient sensory inputs. Could this cluster be used to predict trial outcome at the onset response? Could it be used to predict the presence of the sound, and with which accuracy. The authors discuss a bit the different cluster type, but in a very elusive manner. I recognize that one should be careful with the use of signal analysis methods in calcium imaging but a simple linear deconvolution of the calcium dynamic who help to illustrate the conclusions that the authors propose based on peak responses. It would also be very interesting to align the clusters responses (deconvolved) to the timing of licking and rewards event to check if some clusters do not fire when mice perform licks before the sound comes. It would help clarify if the behavioral signals described here require both the presence of the sound and the behavioral action or are just the reflection of the motor command. As noted by the authors, some clusters have late peak responses (2 and 5). However, 2 and 5 are not equivalent and a deconvolution would evidence that much better. 2 has late onset firing. 5 has early onset but prolonged firing.

We agree with the reviewer’s statement that “cluster 3 is obviously mainly sensory driven”. In the Discussion we refer to cluster 3 as having a “largely behaviorally invariant response profile to the auditory stimulus” (line X), which is consistent with the statement of the reviewer. With regard to the reviewer’s suggestion to describe the “functional differences” between the clusters, we would like to refer to the subsequent three sentences of the same paragraph in which we speculate on the cognitive and behavioral variables that may underlie the response profiles of different clusters. Given the limitations imposed by the task structure, we do not think it is justified to expand on this.

We have added an additional analysis in order to explicitly address the question of which neurons are sound responsive (please also see response to point 3 below and to point 1 of reviewer #2). That trial outcome could be predicted on the basis of only the sound-responsive neurons’ activity during the initial period of the trial (“predict trial outcome at the onset response”) is unlikely given their small number (only 97 of 2649 neurons show a statistically significant sound-evoked response) and given that only a minority (42/98) of those sound-driven neurons are also modulated by trial outcome within that initial trial period (i.e. 0-1s after stimulus onset; data not shown).

Changes to manuscript.

Line 219: “..., while only a small fraction (97 / 2649) exhibited a significant response to the sound.”

Line 658: “Sound-driven neurons were identified by comparing the mean miss trial activity before and after stimulus presentation. Specifically, we performed a Mann-Whitney U test to assess whether there was a statistically significant difference (Benjamini-Hochberg adjusted p-value of 0.05) between the mean activity over the 2 seconds preceding the stimulus and the mean activity over the 1 second period following stimulus presentation. This analysis was performed using miss trials with click intensities from 53 dB SPL to 65 dB SPL (many sessions contained very few or no miss trials at higher sound levels).”

While calcium traces represent an indirect measure of neural activity, deconvolution does not necessarily provide an accurate picture of the spiking underlying those traces and has the potential to introduce additional problems. For instance, deconvolution algorithms tend to perform poorly at inferring the spiking of inhibited neurons (Vanwalleghem et al., 2021). Given that suppression is such a prominent feature of IC activity and is evident both in our calcium data as well as in the electrophysiology data of others (Franceschi and Barkat, 2021), we decided against using deconvolved spikes in our analyses. See also the side-by-side comparison below of the hit and miss trial activity of one example neuron based on either the calcium trace (left) or deconvolved spikes (right) (extracted using the OASIS algorithm (Friedrich et al., 2017) incorporated into suite2p (Pachitariu et al., 2016).

Author response image 1.

(3) Along the same line, the very small proportion of really sensory driven neurons (cluster 3) is not discussed. Is it what on would expect in typical shell or core IC neurons?

As requested by reviewer #2 and mentioned in response to the previous point, we have now quantified the number of neurons in the dataset that produced significant responses to sound (97 / 2649). For a given imaging area, the fraction of neurons that show a statistically significant change in neural activity following presentation of a click of between 53 dB SPL and 65 dB SPL rarely exceeded ten percent. While that number is low, it is not necessarily surprising given the moderate intensity and very short duration of the stimuli. For comparison: Using the same transgenics, labeling approach and imaging setup and presenting 200-ms long pure tones at 60 dB SPL with frequencies between 2 kHz and 64 kHz, we typically find that between a quarter and a third of neurons in a given imaging area exhibit a statistically significant response (data not shown).

Changes to manuscript.

Line 219: “..., while only a small fraction (97 / 2649) exhibited a significant response to the sound.”

Line 658: “Sound-driven neurons were identified by comparing the mean miss trial activity before and after stimulus presentation. Specifically, we performed a Mann-Whitney U test to assess whether there was a statistically significant difference (Benjamini-Hochberg adjusted p-value of 0.05) between the mean activity over the 2 seconds preceding the stimulus and the mean activity over the 1 second period following stimulus presentation. This analysis was performed using miss trials with click intensities from 53 dB SPL to 65 dB SPL (many sessions contained very few or no miss trials at higher sound levels).”

Line 220: “While the number of sound-responsive neurons is low, it is not necessarily surprising given the moderate intensity and very short duration of the stimuli. For comparison: Using the same transgenics, labeling approach and imaging setup and presenting 200-ms long pure tones at 60 dB SPL with frequencies between 2 kHz and 64 kHz, we typically find that between a quarter and a third of neurons in a given imaging area exhibit a statistically significant response (data not shown).”

(4) In the discussion, the interpretation of different transient and permanent cortical inactivation experiment is very interesting and well balanced given the complexity of the issue. There is nevertheless a comment that is difficult to follow. The authors state:

If cortical lesioning results in a greater weight being placed on the activity in spared subcortical circuits for perceptual judgements, we would expect the accuracy with which trial-by-trial outcomes could be read out from IC neurons to be greater in mice without auditory cortex. However, that was not the case.

However, there is no indication that the activity they observe in shell IC is causal to the behavioral decision and likely it is not. There is also no indication that the behavioral signals seen by the authors reflect the weight put on the subcortical pathway for behavior. I find this argument handwavy and would remove it.

While we are happy to amend this section, we would not wish to remove it because a) we believe that the point we are trying to make here is an important and reasonable one and b) because it is consistent with the reviewer’s comment. Hopefully, the following will make this clearer: In order for the mouse to make a perceptual judgment and act upon it - in the context of our task, hearing a sound and then licking a spout - auditory information needs to be read out and converted into a motor command. If the auditory cortex normally plays a key role in such perceptual judgments, cortical lesions would require the animal to base its decisions on the information available from the remaining auditory structures, potentially including the auditory midbrain. This might result in a greater correspondence between the mouse’s behavior and the neural activity in those structures. That we did not observe this outcome for the IC could mean that the auditory cortex did not contribute to the relevant perceptual judgments (sound detection) in the first place. Therefore, no reweighting of signals from the other structures is necessary. Alternatively, greater weight might be placed exclusively on structures other than the auditory midbrain, e.g. the thalamus. The latter would imply that the contribution of the IC remains the same. This includes the possibility that the IC shell does not play a causal role in the behavioral decision – in either control mice or mice with cortical lesions – as suggested by the reviewer.

Changes to manuscript.

Line 471: “This could imply that, following cortical lesions, greater weight is placed on structures other than the IC, with the thalamus being the most likely candidate, ..”

(5) In Fig. 5 the two colors used in B and C are the same although they describe different categories.

The dark green and ‘deep orange’ we used to distinguish between non-lesioned and lesioned in Figure 5C are slightly lighter than the colors used to distinguish between these two categories in other figures and therefore might be more easily confused with the blue and red in Figure 5B. This has been changed.

Author response:

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

We have made revisions accordingly. The following is a list of the changes we have made in this revised Version of Record:

(1) We have added three more panels to Figure 1-figure supplement 1, showing that lipopolysaccharide-induced severe lung injury also generate some ectopic tuft cells expressing both Dclk1 and Gα-gustducin, a G protein α subunit expressed in taste bud cells and many tuft cells.

(2) We have added a new supplemental figure, Figure 2-figure supplement 1, showing the reanalysis data of the single-cell RNAseq dataset (GSE197163) indicating the numbers of Trpm5-GFP+ ectopic tuft cells expressing Tas2r108, Tas2r105, Tas2r138, Tas2r137 and other Tas2rs, respectively. And the original “Figure 2-figure supplement 1” in the previous version has been changed to “Figure 2-figure supplement 2”.

(3) We have added another new supplemental figure, Figure 3-figure supplement 1, showing the H1N1 infection-damaged lung tissue volumes in the Gng13-cKO mice are significantly greater than those in WT or Trpm-/- mice, which is in agreement with the data of the injured lung surface areas from these three genotypes of mice (Figure 3 C and D). And the original “Figure 3-figure supplement 1” in the previous version has been changed to “Figure 3-figure supplement 2”.

(4) We have added to the new Figure 3-figure supplement 2 two new panels: I and J, showing the reanalysis data of the single-cell RNAseq dataset (GSE197163), indicating that about 57% of Trpm5-GFP+ ectopic tuft cells express Gγ13, some of which express Alox5, a key enzyme to the biosynthesis of pro-resolving mediators.

(5) We have added one reference on Sytox and another on Alox5.

(6) We have corrected two labeling errors to Figure 3 G and M, and some other typos in the article. Also, we have removed “Present address” attached to some authors since no present address was needed at all.

Attached below is our point-by-point reply to the comments and suggestions made by the reviewers. We hope that you and the reviewers will find all concerns satisfactorily addressed.

Responses to public reviews:

Reviewer #1:

Li et al. report here on the expression of a G-protein subunit Gng13 in ectopic tuft cells that develop after severe pulmonary injury in mice. By deleting this gene in ectopic tuft cells as they arise, the authors observed worsened lung injury and greater inflammation after influenza infection, as well as a decrease in the overall number of ectopic tuft cells. This was in stark contrast to the deletion of Trpm5, a cation channel generally thought to be required for all functional gustatory signaling in tuft cells, where no phenotype is observed. Strengths here include a thorough assessment of lung injury via a number of different techniques. Weaknesses are notable: confusingly, these findings are at odds with reports from other groups demonstrating no obvious phenotype upon influenza infection in mice lacking the transcription factor Pou2f3, which is essential for all tuft cell specification and development. The authors speculate that heterogeneity within nascent tuft cell populations, specifically the presence of pro- and anti-inflammatory tuft cells, may explain this difference, but they do not provide any data to support this idea.

We thank the reviewer for pointing out the strengths of this work. The phenotypes of the Gng13 conditional knockout mice upon severe pulmonary injury seem to be severer than those of Trpm5 knockout or Pou2f3 knockout mice, which we would attribute to functionally specific tuft cell subtypes. In the intestines, tuft cells are known to promote type II innate immune responses. Those ectopic pulmonary tuft cells emerge at 12 days post infection, and may not be involved in the initial immune responses to the infection, and instead, some of them may contribute to the inflammation resolution and functional recovery. Reanalysis of the previously published single tuft cell RNAseq dataset indeed showed that Gng13 is expressed in a subset of these ectopic pulmonary tuft cells, and anti-inflammatory genes such as Alox5 are also found in some of these tuft cells (please see the newly added Figure 3 supplement 2 I and J). Together, these data suggest that while some of these tuft cells may still play a pro-inflammatory role as in the intestines, some other Gγ13-expressing tuft cells contribute to the inflammation resolution, and disruption of the latter’s function results in the severer phenotypes.

Reviewer #2:

The study by Li et al. aimed to demonstrate the role of the Gγ13-mediated signal transduction pathway in tuft cell-driven inflammation resolution and repairing injured lung tissue. The authors showed a reduced number of tuft cells in the parenchyma of Gγ13 null lungs following viral infection. Mice with a Gγ13 null mutation showed increased lung damage and heightened macrophage infiltration when exposed to the H1N1 virus. Their further findings suggested that lung inflammation resolution, epithelial barrier, and fibrosis were worsened in Gγ13 null mutants.

Strengths:

The beautiful immunostaining findings do suggest that the number of tuft cells is decreased in Gr13 null mutants.

Weaknesses:

The description of phenotypes, and the approaches used to measure the phenotypes are problematic. Rigorous investigation of the mouse lung phenotypes is needed to draw meaningful conclusions.

Thank the reviewer for pointing out the major findings and strengths of our work. Regarding the approaches used to measure the phenotypes, we first did double immunostaining and validated that the lipopolysaccharide-induced DCLK1+ positive cells are indeed ectopic pulmonary tuft cells with an antibody to Gα-gustducin, a commonly expressed G protein α subunit in taste buds and tuft cells. Second, in addition to the measurements of the injured lung surface areas, we determined the injured lung tissue volumes by slicing the injured lungs into a series of tissue sections, quantifying the injured areas in each section and then reconstructing the injured volumes. Third, we reanalyzed the previously published single-tuft cell RNAseq dataset and found that a subset (i.e., ~57%) of Trpm5-GFP+ tuft cells express Gng13, some of which express anti-inflammatory genes such as Alox5. These additional data further support our finding that a subset of these Gγ13-expressing ectopic tuft cells may contribute to the inflammation resolution while others may play a proinflammatory role.

Reply to the recommendations of Reviewer #1:

(1) A major issue with this study is the fact that Chat-Cre mediated knockout of Gng13 leads to reduced tuft cells and impaired recovery, yet global TRPM5 deletion (this study) and global Pou2f3 deletion (Barr et al.) exhibit no apparent phenotype. One can imagine a Trpm5-independent role of Gng13 in tuft cells, but it is much harder to reconcile with the fact that Pou2f3 KO mice, which lack tuft cells entirely, exhibit no apparent phenotype. This was examined in some detail in Barr et al., demonstrating no apparent change in weight loss, dysplastic expansion (Krt5+ cells), or goblet cell metaplasia. The most parsimonious explanation is that Gng13 deletion in another Chat+ cell type, probably neurons of some sort, is leading to this phenotype. The authors really need to investigate this in some detail as the data does not really support a role of tuft cells in the phenotype they observe. Better yet, identification of the other Chat+ cell type in which Gng13 deletion promotes impaired lung recovery would be very interesting. While neurons seem likely, perhaps there is another Chat+ cell type expressing Gng13 in the respiratory tract that could be playing a role as well. In either case, the discrepancy between Pou2f3 KO (no phenotype) and Chat-Cre / Gng13 KO (impaired recovery) is difficult to reconcile.

We agree with the reviewer, and it took us some time to make senses of the data as well. The differences in phenotypes between Trpm5-knockout versus Gng13 conditional knockout (Gng13-cKO) could be explained by that Gγ13 is a partner of Gβγ moiety of a heterotrimeric G protein (Gαβγ)，which is known to act on many effector enzymes and ion channels, while Trpm5 largely regulates the influx of monovalent cations, depolarizing the plasma membrane potentials. Thus, it is understandable that nullification of Gng13 may have more profound effect on cell physiology and consequent phenotypes than that of Trpm5, and similar differential effects were also found in the intestines (Frontiers in Immunology, 2023, DOI 10.3389/fimmu.2023.1259521).

Data from several research groups have indicated that there are subtypes of tuft cells, each of which displays unique gene expression patterns as well as input and out signal profiles. It is yet not well understood how each subtype may contribute to the inflammatory responses or inflammation resolution. Comparative analyses of our data from the Gng13-cKO mice versus those from Pou2f3-KO mice suggest that Gng13-expressing tuft cells may have a role in the inflammation resolution while other ectopic tuft cells may contribute to the maintenance of the inflammation at a certain level, impairing subsequent tissue repairing and recovery. The exact molecular and cellular mechanisms are to be revealed in our future studies.

The central nervous system may also play a role in the impaired lung recovery. But our detailed immunochemical studies did not identify any significant number of neurons innervating the lung tissue co-expressing ChAT and Gng13, suggesting that no immediate action from these neurons may regulate the pulmonary inflammation resolution or functional recovery.

Together, our data suggest the importance of tuft cell subtype-specific functions, which may help us further understand the role of these rare tuft cells.

(2) Figures showing alternative injury models inducing the generation of ectopic tuft cells are not convincing and not quantified. DCLK1 can be a bit promiscuous, so verifying tuft cell expansion in these other models with other markers (especially for LPS and HDM which have not been reported elsewhere) is important.

We agree with the reviewer that DCLK1 is not a very specific marker for tuft cells. We have also observed that chemical inductions of these ectopic tuft cells with bleomycin, HDM or LPS are not as effective as H1N1 viruses. To verify that these rare DCLK1-positive cells are indeed tuft cells, we performed double immunostaining with antibodies to DCLK1 and to Gα-gustducin, another tuft cell marker. The results showed that some of these spindle-shaped DCLK1 positive cells indeed also express Gα-gustducin (see the newly added panels in Figure 1-figure supplement 1), indicating that they are most likely the chemically induced ectopic tuft cells. We also agree with the reviewer that it would be important to further investigate the possible roles of these cells during the stages of the chemically induced injury, inflammation resolution and functional recovery.

(3) Calcium responses in isolated post-flu tuft cells are interesting but difficult to interpret as presented. Can higher-power images be shown? Also, no statistical analysis is presented to provide any confidence in that data.

Thank the reviewer for the suggestions. As found in taste buds, only a subset of these ectopic tuft cells expresses Tas2rs, and each of these cells may express a few of the 35 murine Tas2rs. Thus, a particular bitter tasting compound can activate only few tuft cells and we had to use low-magnification to include more responsive cells in a field under the imaging microscope. We agree with the reviewer that it would be an interesting idea to statistically correlate the response profile to bitter substances with the cell’s Tas2r expression pattern, which we have done with sperm cells before (Molecular Human Reproduction, 2013, doi:10.1093/molehr/gas040). However, the main focus of this work is on the effect of Gng13-cKO in a subset of these ectopic tuft cells on the recovery. We plan to investigate these interesting cells in more details in the future.

(4) I am unaware of Sytox being a specific dye for pyroptotic cells. Can the authors please provide a reference or otherwise justify this?

Sytox is a dye to stain dead cells, which has been used previously in the studies on gasdermin-mediated lytic cell death (Xi et al., Up-regulation of gasdermin C in mouse small intestine is associated with lytic cell death in enterocytes in worm-induced type 2 immunity. PNAS 2021 118(30) e2026307118 https://doi.org/10.1073/pnas.2026307118). In our work we used the dye for the same assay.

(5) The authors perform qPCR for various taste receptor genes pre- and post-flu, but do not show that these genes are specifically induced in tuft cells. Since single-cell data and bulk RNA-Seq are available from Barr et al., the authors should validate the expression of these Tas2r genes specifically in post-flu tuft cells.

Thank the reviewer for the suggestion. Yes, we have performed analysis of the single-cell RNAseq dataset (GSE197163, Barr et al. 2022) and found that among 613 Trpm5-GFP+ tuft cells, Tas2r108 was expressed in the greatest number of cells, i.e., 67 cells, followed by Tas2r105, Tas2R138, Tas2r137, Tas2r118 and Tas2r102, which were detected in 11, 10, 10, 5 and 4 cells, respectively (see the newly added Figure 2-figure supplement 1). This order of expressing cell numbers is very much in agreement with that of the relative Tas2r expression levels obtained with the qPCR experiment (Figure 2A), indicating the expression of these Tas2rs likely in the ectopic tuft cells. We will further validate the data by analyzing the bulk RNA-Seq dataset when it is accessible to us.

(6) Some general editing of language throughout would be helpful to increase readability.

Thanks for pointing out. We have carefully checked the manuscripts, corrected some typos and revised several sentences to increase its readability.

(7) For the fibrosis analysis, trichrome staining is very heterogenous, which is reflected by the large error bars in Fig. 8B. A more quantitative, "whole lung" analysis such as hydroxyproline content or western blotting for Col1a1 would be ideal.

The approach of Masson’s trichrome staining along with qRT-PCR assays on the fibrotic gene expression has been used previously to quantitatively analyze fibrosis (e.g., Zhang et al., Neuropilin-1 mediates lung tissue-specific control of ILC2 function in type 2 immunity. Nature Immunology 23:237-250, 2022, https://doi.org/10.1038/s41590-021-01097-8). We agree with the reviewer that there are large error bars in Fig. 8B, and hydroxyproline content assay or western blotting for Col1a1 would be ideal. But our qRT-PCR was performed on the RNA samples extracted from the “whole lungs”, and its data are also able to reflect the extent of fibrosis of the lungs.

(8) The authors claim that only a subset of tuft cells express Gng13, but this is supported only by a single IF image in Fig. 3 supplement 1G. The authors could download the single-cell dataset from Barr et al. to confirm the heterogeneity of Gng13 expression and get a better sense of the fraction of total ectopic tuft cells that express this, as it is a critical point in their model.

Thank the reviewer for the suggestion. Yes, we have downloaded and reanalyzed the single-cell RNAseq dataset (GSE197163), and found that out of 613 Trpm5-GFP+ tuft cells, 350 or 57% of these cells expressed Gng13 (Figure 3-figure supplement 2I). This result, together with our immunohistochemical data (Figure 3-figure supplement 2G and H) indicates that Gγ13 is expressed in a subset of these ectopic tuft cells. More comprehensive studies are needed to characterize these tuft cell subtypes and elucidate subtype-selective functions.

Reply to the recommendations of Reviewer #2:

The study needs more rigorous examinations of the phenotypes. For example, quantification of the injury area in Fig3C is problematic. Similarly, fibrotic phenotype and quantification in Fig 8C also have problems. This study heavily used qRT-PCR analysis to quantitate the level change of bitter/other receptors in a minor population of tuft cells which are also minor in a whole lung. Given the limited number of cells, it is difficult to appreciate that qRT-PCR can pick up the difference. In addition, how would the findings in this study reconcile with the finding by Huang (PMID: 36129169) where pou2f3 null mutants (without tuft cells) were used? Huang et al. did not observe more severe phenotypes in the mice without tuft cells than controls.

Thank the reviewer for the recommendations. Regarding Fig 3C, please see the reply below: revisions for clarity point #2.

Fig 8 B and C used Masson’s trichrome staining to quantitatively analyze fibrosis, which has been used by other groups as well (e.g., Zhang et al., Neuropilin-1 mediates lung tissue-specific control of ILC2 function in type 2 immunity. Nature Immunology 23:237-250, 2022, https://doi.org/10.1038/s41590-021-01097-8). Our qRT-PCR data on the fibrotic gene expression (Figure 8A) further support the Masson’s trichrome staining results.

We realized that tuft cells make up only a minor population in the lungs. So, we performed qRT-PCR assays on the RNA samples isolated from mostly the injured tissues along with the corresponding tissues from the uninjured lungs as control. To validate our qRT-PCR data, we reanalyzed the previously published single ectopic tuft cell RNAseq dataset (GSE197163), and found that the most abundantly expressed Tas2r108 determined by qRT-PCR was also expressed in the greatest number of tuft cells, and the order of expression levels of other Tas2rs are also well in agreement between the qRT-PCR and single-cell RNAseq data (Figure 2A, Figure 2-figure supplement 1), cross-validating the data obtained by these two very different approaches.

We have carefully studied the finding by Huang (PMID: 36129169). Our data suggest that there are subtypes of the ectopic tuft cells, some of which contribute to the inflammation resolution while others play a proinflammatory role. Indeed, the reanalysis of the aforementioned single tuft cell RNAseq dataset found that about 57% Trpm5-GFP+ ectopic tuft cells expressed Gng13, and some of which expressed Alox5, a key enzyme to the biosynthesis of pro-resolving mediators. Thus, in the Pou2f3-knockout mice, both pro- and anti-inflammatory tuft cells are ablated, it would be hard to observe any significant phenotypes. When the function of a subset of Gγ13-expressing tuft cells is disrupted, the anti-inflammatory role from these cells is eliminated, resulting severer phenotypes. More studies are needed to further understand the subtype-specific functions of these fascinating tuft cells.

Do Gγ13 null mutants show similar phenotypes in bleomycin injury model?

Bleomycin and other chemicals-induced injury models indeed engender much fewer ectopic pulmonary tuft cells. Thus, it is more difficult to test the effect of Gng13 mutation due to the small number of the Gng13-expressing tuft cells in either WT or mutant lungs.

What is the cell fate of lineage labeled tuft cells in the lungs of Chat-Cre:Ai9:Gng13flox/flox mice following viral infection at different times examined? The numbers were decreased at different time points post-injury based on the data. Did these cells undergo apoptosis? It is an excellent idea to look into the cell fate of ChAT-Cre:Ai9:Gng13flox/flox. We believe that these cells would have a similar fate to other ectopic tuft cells, probably undergoing apoptosis. But our data suggest that Gng13 mutation suppresses the increase the ectopic tuft cells, or the increase of a particular subtype of these tuft cells. Further studies are needed to elucidate the molecular mechanisms of the Gγ13-mediated signal transduction pathways regulating the proliferation of a subset of ectopic tuft cells.

Here are the revisions for clarity and coherence to the figures:

(1) Fig 2: For the functional assessment, using tracheal tuft cells from the same ChAT-Cre:Ai9 mice would be a suitable positive control in the calcium response traces experiment. These specific cells could also serve as a control in Fig2a.

We would agree with the reviewer that tracheal tuft cells from the same ChAT-Cre: Ai9 mice would be an ideal positive control in the calcium response experiment as well as in the qRT-PCR assay. But we have established reliable methods to calcium image primary cells expressing taste receptors and quantify their RNA expression levels, which have been used in our previous publications, e.g., (1) Functional characterization of bitter taste receptors expressed in mammalian testis. Molecular Human Reproduction, 2013, doi:10.1093/molehr/gas040; (2) Infection by the parasitic helminth Trichinella spiralis activates a Tas2r-mediated signaling pathway in intestinal tuft cells. PNAS 2019, www.pnas.org/cgi/doi/10.1073/pnas.1812901116. We thank the reviewer for the excellent suggestion.

(2) Fig 3C: It is not clear whether the depicted areas really represent the injured area. To provide a more comprehensive view, the authors should also provide histological analysis and quantification of the injured lung. A 3D representation of the injury area would offer a more accurate presentation.

Thank the reviewer for the point. The depicted areas in Fig 3C are indeed the injured surface areas of the lungs. Following the reviewer’s suggestion, we carried out the histological analysis to determine the injured tissue volumes of the lungs. We fixed the lungs, and sliced them into 12 μm-thick sections, which were imaged under a microscope. The injured areas in a section were identified and quantified using the ImageJ software, and then the injured volume for this section was obtained by multiplying the area by the thickness of the section, i.e., 12 μm. Statistical analyses indicate that the injured volume of the Gng13-cKO lungs is significantly more than those of WT or Trpm5-KO mice, which has been included in Figure 3-figure supplement 1, and is in agreement with the data of the injured surface areas (Fig 3C).

(3) Fig 3 G/I/K/M: There seems to be an inconsistency in the time points. There's no indication for 14 dpi, yet two for 25 dpi. Additionally, a color legend for each sample would be helpful.

Thank the reviewer for pointing out. There were two typos, which have been corrected. Yes, the time points should be 14 dpi, 20 dpi, 25 dpi and 50 dpi. And a color legend has been added as well.

(4) Fig 4A: Using CD64 co-stained with Krt5 might better highlight the immune cells in the damaged region. Additionally, could you clarify the choice of the neutrophil marker CD64 over CD45 for staining the injured lung?

We agree with the reviewer that Krt5 antibody staining can help define the damaged region. We sectioned the lung tissues with a special attention to the damaged areas, but we found that the adjacent healthy areas also had extra immune cells. Thus, we counted in all these CD64+ cells in both the damaged as well as the surrounding, seemingly healthy areas. We used CD64 instead of CD45 to label these altered immune cells because we found that CD64 can better label the differential immune cells between WT and Gng13-cKO mice following H1N1 infection. Furthermore, CD64-labeled cells could be readily related to the Gsdmd/Gsdme-expressing F4/80-labeled immune cells shown in Figure 5 and its supplemental figures.

(5) Fig 5 and Supplemental Fig 5: It appears that the F4/80 staining exhibits notable background staining.

Yes, there is some background staining. The antibody was the best we could find, but its quality could be further improved. On the other hand, we thought that there were some cellular debris that might be stained positive by that antibody. At a higher magnification, however, we could still identify individual cells co-expressing IL-1β.

(6) Fig 8C: The depicted area does not seem to adequately represent the fibrosis in the injured lung.

Masson’s trichrome staining has been previously used to quantitatively analyze fibrosis (e.g., Zhang et al., Neuropilin-1 mediates lung tissue-specific control of ILC2 function in type 2 immunity. Nature Immunology 23:237-250, 2022, https://doi.org/10.1038/s41590-021-01097-8). Our qRT-PCR assays on the fibrotic gene expression (Figure 8A) were performed on the RNA samples extracted from the whole lungs, and the resultant data are able to reflect the extent of fibrosis of the lungs, although we also agree with the reviewer that additional data would make the conclusion more convincing.

Author response:

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

We express our sincere appreciation for your insightful comments and constructive suggestions. It is with great pleasure that we submit the revised version of our manuscript. Over the past months, we have meticulously considered all the invaluable feedback provided by the three anonymous reviewers, and endeavored to incorporate significant revisions accordingly. Furthermore, we have meticulously rephrased the results section in accordance with your guidance, aiming to bolster the rigor of our manuscript. The specific changes implemented in the revised manuscript are outlined below:

- Revised the title of the manuscript.

- Revised the description of early mitotic and meiotic chromosome structure in the scc3 mutant (Lines 167-274).

- Added the BiFC results illustrating the interaction between SCC3 and other cohesin proteins in Figure S10.

- Enhanced the detail in the description of figure legends, particularly for Figures 2 and 4.

- Refined and rephrased the language of the manuscript.

We hope these positive revisions have substantially strengthened the manuscript. Once again, we extend our heartfelt gratitude for your invaluable input.

eLife assessment

This important study elucidates the function of the cohesin subunit SCC3 in impeding DNA repair between inter-sister chromatids in rice. The observation of sterility in the SCC3 weak mutant prompted an investigation of abnormal chromosome behavior during anaphase I through karyotype analysis. While the evidence presented is largely solid, the strength of support can be substantially improved in some aspects, leaving room for further investigation. This research contributes to our understanding of meiosis in rice and attracts cell biologists, reproductive biologists, and plant geneticists.

Public Reviews:

Reviewer #1 (Public Review):

The manuscript describes the identification and characterization of rice SCC3, including the generation and characterization of plants containing apparently lethal null mutations in SCC3 as well as mutant plants containing a c-terminal frame-shift mutation. The weak scc3 mutants showed both vegetative and reproductive defects. Specifically, mitotic chromosomes appeared to partially separate during prometaphase, while meiotic chromosomes were diffuse during early meiosis and showed alterations in sister chromatid cohesion, homologous chromosome pairing, and recombination. The authors suggest that SCC3 acts as a cohesin subunit in mitosis and meiosis, but also plays more functions other than just cohesion.

Reviewer #2 (Public Review):

This manuscript shows detailed evidence of the role of cohesin regulators in rice meiosis and mitosis.

Reviewer #3 (Public Review):

Prior research on SCC3, a cohesin subunit protein, in yeast and Arabidopsis has underscored its vital role in cell division. This study investigated into the specific functions of SCC3 in rice mitosis and meiosis. In a weakened SCC3 mutant, sister chromatids separating was observed in anaphase I, resulting in 24 univalents and subsequent sterility. The authors meticulously documented SCC3's loading and degradation dynamics on chromosomes, noting its impact on DNA replication. Despite the loss of homologous chromosome pairing and synapsis in the mutant, chromosomes retained double-strand breaks without fragmenting. Consequently, the authors inferred that in the scc3 mutant, DNA repair more frequently relies on sister chromatids as templates compared to the wild type.

We extend our sincere gratitude to the Editors and the Reviewers for their highly constructive and insightful suggestions. We deeply appreciate receiving both positive feedback and constructive criticism on our manuscript. In light of the reviewers’ comments, we have diligently undertaken substantial revisions to improve the manuscript. The revised version comprehensively addresses all the points raised by the reviewers.

Below, we provide a detailed point-by-point response to the reviewers’ comments:

Recommendations for the authors:

Reviewer #1:

(1) Line 170- looking at pollen formation does not specifically evaluate whether SCC3 is involved in meiosis.

Thank you very much for this advice. We totally agree with your point of view that pollen formation defects only indicate the problem of gametogenesis. We are sorry for not accurately describing this sentence. It has been revised in the manuscript (Lines 167-176).

(2) Lines 203-205- this seems more like discussion and is pure speculation. Another possibility described above is that the truncated SCC3 protein is partially functional and what they see is due to this partial functionality. Have the authors considered the possibility that a partially functional version of SCC3 is produced that alters its function or the function of the cohesin complex? How much of the protein epitope remains in the truncated protein?

We are so grateful for the insightful suggestions provided. We concur with the proposition that a partially functional SCC3 may indeed be synthesized, contributing to the survivability of the mutant. Notably, the truncated version of the protein retains approximately 60% to 70% of the epitope, which ostensibly maintains a residual functionality within the weak scc3 mutant. In this manuscript, the loss of C-terminal 910-1116 aa of SCC3 contains a special protein epitope and a certain protein secondary structure, which may alter the protein’s folding and its subsequent roles within the cohesin complex.

In this study, we encountered challenges in generating null alleles of the scc3 mutants in rice utilizing the CRISPR-Cas9 system. Consequently, it is plausible that the scc3-1 and scc3-2 variants represent null alleles of SCC3, resulting in embryonic lethality. We posit that the identification of weak alleles is paramount to facilitating the survival of the organism. Thus, selecting some weak mutants, particularly those exhibiting the most pronounced phenotype, is advantageous for conducting further research. Our findings indicate that the diminished scc3 mutant lacks only a segment of the C-terminal, yet this deficiency is adequate to ensure the plant's survival while significantly impeding the meiotic process. We cannot dismiss the likelihood that these observed defects are attributable to the unique truncated proteins. We extend our sincerest thanks once again.

(3) Lines 212- I question whether what the authors see in Figure 2 is chromosome fragmentation. It could just as well be alterations in chromosome structure. Likewise, the authors provide little to no evidence that the mutation affects the replication process. Rather, the presence of replicated chromosomes later in mitosis and meiosis would argue that replication is not disrupted.

We express our gratitude to the reviewer for highlighting this critical inquiry. Contrary to the scenario of chromosome fragmentation, as you astutely observed, the preservation of normal sister chromatids during prometaphase indicates that the replication process remains uninterrupted. In alignment with your insights, our study embarked on an extensive series of full-length fluorescence in situ hybridization (FISH) experiments to elucidate the underlying mechanisms contributing to the observed increase in the distance between sister chromatids, particularly during interphase. The preponderance of our findings corroborates the hypothesis that the chromosomes exhibit alterations in structure, as depicted in Figure 2A. Intriguingly, our data suggest that cohesin, upon interaction with other chromatin-bound proteins, may facilitate loop extrusion, anchoring itself in a manner that potentially alters chromosomal architecture. These alterations in chromosome structure and the subsequent defects in genome folding and cohesion establishment, particularly rely on SCC3. In response to your valuable suggestions, we have meticulously revised the relevant sections of our manuscript. We extend our sincere thanks for your insightful comments.

(4) Line 230- what does the sentence SCC3 may enhance the interaction with DNA mean, the interaction of the cohesin complex?

We are sorry for the ambiguity in our initial description and wish to clarify that SCC3 indeed plays a pivotal role in augmenting the interaction between the cohesin complex and DNA. Our observations revealed an upsurge in the signal intensity of SCC3 as cells transition from interphase to prophase, as depicted in Figure 2B. This enhancement correlates with the observed defects in scc3 mutants during prophase, suggesting that SCC3’s functional significance is particularly pronounced at this stage of the cell cycle. We have revised our manuscript to reflect these insights more accurately, in accordance with your valuable suggestions. We express our sincere gratitude for your guidance.

(5) Oddly, and unexplainably the authors present data indicating that SCC3 interacts with RAD21.1, but not SMC1, SMC3, or REC8. The fact that the authors report that SCC3 only interacts with RAD21.1 but no other cohesin proteins is quite hard to explain.

As argued in the point above, the available data do not provide compelling evidence supporting the interaction between SCC3 and other cohesin proteins. We have repeated yeast two-hybrid (Y2H) experiments yielding consistent outcomes, which also surprised us initially. In the revised manuscript, we further added the bimolecular fluorescence complementation (BiFC) results between SCC3 and other cohesin proteins in rice protoplast (Figure S10). These supplementary data affirm that SCC3 predominantly interacts with RAD21.1, excluding interactions with other cohesin proteins. While the absence of such interactions is perplexing, our investigations have failed to detect any binding between SCC3 and other cohesin proteins.

A weak interaction between SCC3 and REC8 has been reported in Arabidopsis (Kuttig et al. bioRxiv https://doi.org/10.1101/2022.06.20.496767). We speculate that either these proteins do not interact or the yeast-hybrid assays may be inadequate for detecting their interaction, as several factors can impede interaction in a heterologous system. In Figure 7, we could only detect the interaction between SCC3 and RAD21.1 in both Y2H and BiFC experiments. This suggests potential alterations in protein folding or conformation, or the involvement of additional regulatory factors modulating the interaction between SCC3 and other cohesin proteins. Notably, given RAD21.1’s pivotal role as a core component in the cohesin complex, our supplementary findings demonstrate the interactions between SMC1/3 and RAD21.1 (data not shown). Consequently, our current data propose a model wherein RAD21.1 and SMC1/3 form a circular structure, with SCC3 positioned on the outer periphery of the ring complex, associating specifically with RAD21.1 (Figure 8A).

Reviewer #2:

The authors did not consider creating heterozygous mutants for the replication fork. Moderate English language editing may be required.

We extend our gratitude to the reviewer for their valuable suggestions. Initially, we did not explore the potential relationship between SCC3 and the replication fork. Cohesin, as we understand, becomes associated with DNA prior to DNA replication. The phenomenon of sister chromatid co-entrapment arises as replication forks traverse through cohesin rings, a process intricately linked to DNA replication dynamics. In this study, we exclusively observed aberrant chromosome structures in the scc3 mutant during interphase (Figure 2). We conjecture that these anomalies may stem from alterations in chromosome structure, such as genome folding and loop extrusion, rather than being directly attributable to the DNA replication fork. However, the precise nature of these chromosome structural aberrations during interphase in the scc3 mutant remains elusive, necessitating further comprehensive investigation in future studies. We have refined the language of our manuscript in accordance with the reviewer’s suggestions. Once again, we express our sincere appreciation for the invaluable suggestions provided.

Reviewer #3:

While the paper's conclusions are generally well-supported, further substantiation is needed for the claim that SCC3 inhibits template choice for sister chromatids. To bolster this conclusion, I recommend that the authors perform whole-genome sequencing on parental and F1 individuals from two rice variants, subsequently calculating the allele frequencies at heterozygous sites in the F1 individuals. If SCC3 indeed inhibits inter-sister chromatid repair in the wild type, we would anticipate a higher frequency of inter-homologous chromosome repair (i.e., gene conversion). This should be manifested as a bias away from the Mendelian inheritance ratio (50:50) in the offspring of the wild type compared to the offspring of the scc3+/- mutant.

We express our sincere appreciation for your insightful suggestions. It is really a good suggestion. We have arranged to do this experiment. As it takes long time to prepare plant materials and sequence analysis, we hope the ongoing sequencing work will get some important information supporting those hypotheses. As we have not obtained the direct evidence that SCC3 involved in sister chromatid repair, we changed the title as “SCC3 is an axial element essential for homologous chromosome pairing and synapsis”. Once again, we really extend our gratitude for your invaluable suggestions.

A point that warrants consideration is the placement of the protein interaction experiments involving SCC3 within the paper. It is presented relatively late in the manuscript. If the authors possess information regarding the interaction between RAD21.1 and SCC3 and how it relates to the functional study of RAD21.1, it could contribute to a more comprehensive analysis. However, if this information is unrelated to the current study, it might be advisable to omit it, as it appears to diverge from the main focus of this work.

We express our sincere gratitude for your invaluable suggestions. It has been documented in yeast that the interaction between SCC3 and SCC1 is indispensable for the efficient loading of cohesin. In our study, we endeavored to elucidate the intricate relationships among various cohesin subunits. Through our investigations, we have discerned that RAD21.1 serves as a pivotal core subunit within the cohesin complex, facilitating interactions with both SMC1/3 and SCC3 (data not shown). Additionally, our findings indicate that the interaction between RAD21.1 and SCC3 is imperative for maintaining the stability of the cohesin ring and its association with DNA (data not shown). Consequently, the interaction between these two proteins assumes paramount importance for our subsequent analyses. This study holds significant promise for future investigations.

It's worth noting that while the title of the study claims that "SCC3 inhibits inter-sister chromatids repair during rice meiosis," the last sentence of the abstract weakens this conclusion by using the word "seems." A study's title should ideally reflect the most definitive and conclusive findings.

We sincerely appreciate your valuable suggestions. In response, we have revised the description in our manuscript to enhance its rigor.

In Figure 8C, it appears that cohesin is depicted between two DNA strands.

Figure 8C illustrates the process of sister chromatid repair during meiosis in the scc3 mutant. Two gray lines and two blue lines represent the four sister chromatids of two homologous chromosomes, respectively. In the wild type, cohesin plays a crucial role in tethering together the two sister chromatids. As per your reminder, cohesin should indeed encircle the two sister chromatids, as depicted in Figure 8B. Following a thorough evaluation and to mitigate any potential confusion, we have deleted Figure 8C.

Author response:

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

We appreciate your comments and suggestions on our manuscript.

In particular, we have measured the affinity between the middle tail domain of myosin-5a (Myo5a-MTD) and the actin-binding domain of melanophilin (Mlph-ABD) using microscale thermophoresis, and obtained the Kd of ~0.56 uM, which is similar to the Kd of the globular tail domain of myosin-5a (Myo5a-GTD) to the GTD-binding motif of melanophilin (Mlph-GTBM). Moreover, we have performed Western blot of the lysate of transfected cells, showing that the proteins of the dominant negative construct and the negative control were expressed at similar lever without noticeable degradation.

We appreciate the editors’ and reviewers’ comment on how melanophilin might be regulated in binding to the exon-G of myosin-5 and to actin filaments. Phosphorylation of melanophilin by protein kinase A is one possible mechanism. We will investigate this issues in our future study.

We also took this opportunity to correct several minor errors in the manuscript. Textual alterations can be viewed in the “tracked change” version of the manuscript. Below is the comments from the editors and the two reviewers together with our point-by-point responses.

eLife assessment

This study represents a useful description of a third interaction site between melanophilin and myosin-5a which is important in regulating the distribution of pigment granules in melanocytes. While much of the data forms a solid case for this interaction, the inclusion of important controls for the cellular studies and measurement of interaction affinities would have been helpful.

Public Reviews:

Reviewer #1 (Public Review):

Interactions known to be important for melanosome transport include exon F and the globular tail domain (GTD) of MyoVa with Mlph. Motivated by a discrepancy between in vitro and cell culture results regarding necessary interactions for MyoVa to be recruited to the melanosome, the authors used a series of pull-down and pelleting assays experiments to identify an additional interaction that occurs between exon G of MyoVa and Mlph. This interaction is independent of and synergistic with the interaction of Mlph with exon F. However, the interaction of the actin-binding domain of Mlph can occur either with exon G or with the actin filament, but not both simultaneously. These data lead to a modified recruitment model where both exon F and exon G enhance the binding of Mlph to auto-inhibited MyoVa, and then via an unidentified switch (PKA?) the actin-binding domain of Mlph dissociates from MyoVa and interacts with the actin filament to enhance MyoVa processivity.

The only weakness noted is that the authors could have had a more complete story if they pursued whether PKA phosphorylation/dephosphorylation of Mlph is indeed the switch for the actin-binding domain of Mlph to interact with exon G versus the actin filament.

We thank Reviewer #1 for careful reading of the manuscript and appreciation of the study. We agree with the Reviewer that it is important to understand how the actin-binding domain of Mlph switch its interaction with the exon-G of Myo5a and actin filament. We would like to pursue this direction in our future research.

Reviewer #2 (Public Review):

The authors identify a third component in the interaction between myosin Va and melanophilin- an interaction between a 32-residue sequence encoded by exon-g in myosin Va and melanophilin's actin-binding domain. This interaction has implications for how melanosome motility may be regulated.

While this work is largely well done and certainly publishable following needed revisions (e.g. some affinity measurements, necessary controls for the dominant negative experiments), I believe that additional work would be required to make a more compelling case. First, the study provides just one more piece to a well-developed story (the role of exon-F and the GTD in myosin Va: melanophilin (Mlph) interaction), much of which was published 20 years ago by several labs. Second, the study does not demonstrate a physiological significance for their findings other than that exon-G plays an auxiliary role in the binding of myosin Va to Mlph. For example, what dictates the choice between Mlph's actin binding domain (ABD) binding to actin or to exon-G. Is it a PTM or local actin concentration? It is unlikely to be alternative splicing as exon-G is present in all spliced isoforms of myosin Va. And what changes re melanosome dynamics in cells between these two alternatives? Similarly, the paper does not provide any in vitro evidence that binding to exon-G instead of actin effects the processivity of a Rab27a/Myosin Va/Mlph transport complex. For example, if the ABD sticks to exon-G instead of actin, does that block Mlph's ability to promote processivity through its interaction with the actin filament during transport? In summary, given that the authors did not directly test their model either in vitro or in cells, I do not think this story represent a significant conceptual advance.

We thank Reviewer #2 for careful reading of the manuscript and the suggestions of improving the manuscript. As suggested by the reviewer, we have measured the affinity between the middle tail domain of Myo5a (Myo5a-MTD) and Mlph-ABD (Kd ~0.562 uM), which is similar to that between the globular tail domain of Myo5a (Myo5a-GTD) and the GTBM of Mlph. In addition, we have performed additional experiments showing the integrity and the expression level of the dominant negative constructs in the transfected cells.

We believe more extensive experiments are required to address other questions raised by the reviewer. For example, what dictates the choice between Mlph's actin binding domain (ABD) binding to actin or to exon-G is an open question. As we proposed, phosphorylation by protein kinase A is only one possible mechanism. We would like to pursue them in our future research.

Recommendations for the authors:

The reviewing editor feels strongly that addressing some of the points raised by the reviewers would make this a more compelling manuscript. In particular, a measurement of the affinity of the relevant fragments from melanophilin and myosin-5a would indicate that the interaction might be physiologically relevant. Concerning the dominant negative experiments, the lack of effect of an expressed fragment could be that the expressed fragments were simply degraded or expressed at too low of a level to be competing. The reviewer gives guidelines on how to address this. Reviewer #2 made a point that it would be compelling if the effect of phosphorylation as suggested in the model was tested, but we all agree that this could well be the subject of a later study. In addition, the authors make a very interesting proposal for how protein kinase A could be involved in this regulation as has been suggested previously. Perhaps the use of phosphomimetic mutations could give some insight into this. Such experiments, if consistent with the proposed model would certainly raise the impact of this study. Finally, a very clear periodicity in hydrophobic amino acids is apparent in the interacting sequences of both Myo5 (yrisLykrMidLmeqLekqdktVrkLkkqLkvFakkIgeLevgqmen) and Mlph (tdeeLseMedrVamtAseVqqAeseIsdIesrIaaLra). This is strongly suggesting a leucine-zipper-like coiled coil, rather than an interaction mediated solely by charge. Recent softwares (and easily accessible too) like AlphaFold multimer might yield important structural insight into the binding configuration and might help rationalize the effect of the mutations herein.

We thank the editors and the reviewers for their suggestions of improving the manuscript. We have performed the several essential experiments to address the concerns raised by the reviewers.

(1) Regarding the affinity of the relevant fragments from melanophilin and myosin-5a. We have measured the affinity between Mlph-ABD and Myo5a-MTD using MST (Kd ~562 nM) (see revised Figure 3A).

(2) Regarding the concerns on the dominant negative experiments. We have examined the molecular sizes and expression levels of  Mlph or Myo5a constructs by Western blots. First, we show that all constructs have correct molecular size in transfected cells (see revised Figure 6C and 7D), indicating that the inability of Myo5a or Mlph truncations to generate dilute-like phenotypes was not due to the intracellular degradation of the EGFP fusion protein. Second, by correcting for the percentage of transfected cells, we show that the overall expression levels of the wild-type construct and the mutants are roughly equal. Third, we categorized the expression levels into high and low, and calculated percentage of the DN phenotype in high and low expression levels. The results are consistent with the percentage of DN phenotype in total EGFP fusion protein cells.

(3) Regarding the suggestion to investigate the effect of phosphorylation by protein kinase A on Mlph-ABD’s interaction with Myo5a and actin filament. We understand that it is important to elucidate the mechanism by which the actin-binding domain of Mlph switch its interaction with the exon-G of Myo5a and actin filament. However, as we proposed, phosphorylation by protein kinase A is one possible mechanism, and more extensive experiments are required to address this question. Therefore, we would like to pursue it in our future research.

(4) Regarding the suggestion to predict the interaction between the exon-G of myosin-5a and Mlph-ABD using AlphaFold. We have used AlphaFold multimer to predict the Myo5a-MTD/Mlph-ABD interaction. Remarkably, the AlphaFold predicted that the binding of Myo5a-MTD with Mlph-ABD is mediated by an antiparallel coiled-coil formed by Myo5a (1430-1467) and Mlph (450-481), just as predicted by the editors. This prediction is also consistent with our finding that the exon-G of Myo5a interacts with Mlph-ABD. However, the predicted model cannot explain our mutagenesis results. We will pursue this point in the future research. Nevertheless, we are grateful to the editors for bringing this idea to our attention, because it will help us to design experiments to investigate the nature of Myo5a-exon-G/Mlph-ABD interaction.

Reviewer #1 (Recommendations For The Authors):

Specific minor comments

Q1: In figs 6-7 an overlay between DAPI and EGFP would be helpful for the reader to see perinuclear distribution.

As suggested, we have added the merged images of DAPI and EGFP in the revised Figure 6 and 7.

Q2: The delta symbol in the pdf text was corrupted.

The corrupted delta symbol has been fixed in the revised manuscript.

Reviewer #2 (Recommendations For The Authors):

Q1: Please explain in detail early in the text what exon-G is - length, position in the tail, and evidence that it is a coiled coil (CC). Of note, is it only long enough for about 4 heptad repeats? Has it been shown biochemically to form a CC? Is the CC irreversible? What would be the consequence of removing the exon-G CC on the ability of surrounding regions to bind Mlph (exon-F and the GTD)?

We thank the reviewer for this suggestion. In the revision, we added a new paragraph (the first paragraph in the results section) and revised Figure 1A to introduce the middle tail domain and alternatively spliced exons of Myo5a.

Exon-G is 32 amino acids in length, located at the C-terminal region of the middle tail domain, immediately before the globular tail domain. Exon-G region was predicted to form a short coiled-coil by using on-line tools (such as paircoil), and this prediction has not been tested biochemically. Moreover, we do not know whether the exon-G coiled-coil is reversible or not.

We have not examined the effect of removing the whole exon-G on the interaction between the GTD and Mlph-GTBM. The exon-G (residues 1436-1467) and the GTD core (residues 1498-1877) are separated by a long loop of 31 residues. We therefore expect that the removing the exon-G will not affect the GTD/Mlph-GTBM interaction.

Physically, exon-F is immediately followed by exon-G, and those two regions might interfere with each other. In our preliminary study, we found that removing the whole exon-G abolished the interaction between exon-F and Mlph-EFBD. On the other hand, removing the C-terminal half (residues 1454-1467) of exon-G had little effect the interaction between exon-F and Mlph-EFBD (see Figure 2C). In this work, we intentionally selected the later construct for functional analysis of the exon-G/Mlph-ABD interaction, because removing the C-terminal half of exon-G abolishes the interaction with Mlph-ABD, but does not affect the exon-F/Mlph-EFBD interaction.

Q2: Figures 1-3. While the pulldown experiments demonstrating an interaction between Mlph-ABD residues 446-571 and Myo5a-MTD are a good start, one would like to see affinity measurements to gauge the likelihood that this interaction is physiologically relevant. The same goes for the pulldown experiments demonstrating an interaction between (i) the C-terminal half of exon-G (residues 1453-1467) and the Mlph-ABD, (ii) between residues 1411-1467 (a short peptide containing exon-F and exon-G) and the Mlph-ABD, and (iii) between residues 1436-1467 (a short peptide containing exon-G) and the Mlph-ABD. This would also apply to the pulldowns in 3C-3E where versions of the proteins with charge residue changes were tested.

We agree the reviewer’s opinion that determination of the affinities between Mlph-ABD and Myo5a-MTD and their variants will be helpful in understanding the physiological relevance of Exon-G/Mlph-ABD interaction. However, the extensive experiments suggested by the reviewer require many high quality, purified proteins, which are not trivial.

Nevertheless, we think it is important to know the affinity between Myo5a-MTD and Mlph-ABD (both wild-type), as this parameter can be used for the comparison of the three interactions between Myo5a and Mlph. Therefore, we have obtained the affinity between Myo5a-MTD and Mlph-ABD using microscale thermophoresis (MST). The dissociation constant (Kd) of Myo5a-MTD to Mlph-ABD is 0.562±0.169 uM, which is similar to that between Myo5a-GTD and Mlph-GTBM (~1 uM) (Geething & Spudich (2007) JBC 282:21518). Consistent with GST pulldown results, MST shows that deletion of C-terminal half of exon-G (1453-1467) greatly decreases the MST signals (see revised Figure 3A).

Q3: While the domain negative (DN) approach to testing functional significance is OK, rescuing dilute/myosin Va null melanocytes with full-length myosin Va containing the various deletions would have been more convincing. Also, the authors must show (i) that the DN constructs are the correct size in transfected cells (i.e. are not degraded), and (ii) that they are expressed at roughly equal levels (either by doing Westerns and correcting for the percent of transfected cells, or by measuring total cellular fluorescence in transfected cells). Without this information, it remains possible that constructs not exhibiting a DN effect are simply degraded or poorly expressed. This applies to all the DN data in Figures 6 and 7.

We agree with the reviewer that Myo5a null melanocytes is ideal for investigating exon G function. Unfortunately, we do not have Myo5a null melanocytes derived from dilute mice.

To confirm the integrity of the overexpressed proteins in the transfected cells, we performed Western blot of those proteins, including  EGFP-Mlph-RBD (wild-type and two mutants) and Myo5a-Tail (wild-type and G mutant), in the lysate of the transfected cells. Western blots show that all those proteins have correct molecular masses, indicating no degradation of those overexpressed proteins (see revised Figure 6C and 7C). Moreover, by correcting for the percentage of transfected cells, we show that the overall expression levels in each transfected cell of the wild-type construct and the mutants are roughly equal. This information is included in the revised manuscript (Line 222-225; 237-241).

Q4: The authors scored the DN phenotype as yes/no but it mostly likely varies depending on the degree of over-expression. Showing that the degree of melanosome centralization scales with the degree of overexpression, and that the correlation between expression level and phenotype varies depending on the construct would strengthen the results.

We agree with the reviewer’s prediction that the degree of DN phenotype should depend on the of over-expression level. We analyzed the EGFP signals of transfected cells and found very few cells with medium expression level. Therefore, we simply categorized the expression levels into high and low, and calculated the DN phenotype in each categories as shown in the table below. These results are consistent with the expectation that the degree of DN phenotype depends on the over-expression level of the transfected constructs.

Author response table 1.

Percentage of the EGFP-expressing cells with perinuclear aggregation of melanosomes

Q5: The conclusion from the data in Figure 8A- "the presence of both exon-F and exon-G is insufficient for binding to the Mlph occupied by Myo5a, but sufficient for binding to the unoccupied Mlph"- should be verified by also doing the experiment in myosin Va knockdown cells.

We agree. Unfortunately, our RNAi knockdown of Myo5a in melanocytes by RNAi is not ideal and we do not have Myo5a knockout melanocytes. We will pursue this point in the future.

Q6: Line 213 "three Mlph-binding regions, i.e., exon-F, exon-F, and GTD (Figure 7A)" has a typo.

This typo has been corrected.

Q7: The authors should provide high mag insets for the images in Figure 8.

As suggested, we have revised Figure 8 by including high mag insets for the images.

Author response

Reviewer #1 (Public Review):

Summary:

The authors aimed to modify the characteristics of the extracellular matrix (ECM) produced by immortalized mesenchymal stem cells (MSCs) by employing the CRISPR/Cas9 system to knock out specific genes. Initially, they established VEGF-KO cell lines, demonstrating that these cells retained chondrogenic and angiogenic properties. Additionally, lyophilized carriage tissues produced by these cells exhibited retained osteogenic properties.

Subsequently, the authors established RUNX2-KO cell lines, which exhibited reduced COLX expression during chondrogenic differentiation and notably diminished osteogenic properties in vitro. Transplantation of lyophilized carriage tissues produced by RUNX2-KO cell lines into osteochondral defects in rat knee joints resulted in the regeneration of articular cartilage tissues as well as bone tissues, a phenomenon not observed with tissues derived from parental cells. This suggests that gene-edited MSCs represent a valuable cell source for producing ECM with enhanced quality.

Strengths:

The enhanced cartilage regeneration observed with ECM derived from RUNX2-KO cells supports the authors' strategy of creating gene-edited MSCs capable of producing ECM with superior quality. Immortalized cell lines offer a limitless source of off-the-shelf material for tissue regeneration.

We thank the reviewer for the interest in our work. We however want to clarify that the present manuscript does not report the generation of ECM with “superior quality”, but rather of modulated composition and thus function.

Weaknesses:

Most data align with anticipated outcomes, offering limited novelty to advance scientific understanding. Methodologically, the chondrogenic differentiation properties of immortalized MSCs appeared deficient, evidenced by Safranin-O staining of 3D tissues and histological findings lacking robust evidence for endochondral differentiation. This presents a critical limitation, particularly as authors propose the implantation of cartilage tissues for in vivo experiments. Instead, the bulk of data stemmed from type I collagen scaffold with factors produced by MSCs stimulated by TGFβ.

The chondrogenic differentiation of our MSOD-B line and their capacity of undergoing endochondral ossification has been robustly demonstrated in previous studies (Pigeot et al., Advanced Materials 2021 and Grigoryan et al., Science Translational Medicine 2022). In the present manuscript, we thus compare the chondrogenic capacity of newly established VEGF-KO and RUNX-KO lines to those of MSOD-B cells. We demonstrate by qualitative (Safranin-O staining, Collagen type 2 and Collagen type X immuno-stainings) and quantitative (glycosaminoglycans assay) assays that the generated tissues consist in cartilage grafts of similar quality than the MSOD-B counterpart. Of note, the safranin-O stainings were performed on lyophilized tissues, which can alter the staining quality/intensity. We will thus provide additional stainings of generated tissues pre-lyophilization.

The rationale behind establishing VEGF-KO cell lines remains unclear. What specific outcomes did the authors anticipate from this modification?

VEGF is a known master regulator of angiogenesis and a key mediator of endochondral ossification. It has also been extensively used in bone tissue engineering studies as a supplemented factor – primarily in the form of VEGFα – to increase the vascularization and thus outcome of bone formation of engineered grafts (https://www.nature.com/articles/s42003-020-01606-9, https://www.sciencedirect.com/science/article/pii/S8756328216301752). In our study, it was thus identified as a natural candidate to demonstrate the possibility to generate VEGF-KO cartilage and subsequently assess the functional impact on both the angiogenic and osteogenic potential of resulting cartilage tissue.

Insufficient depth was given to elucidate the disparity in osteogenic properties between those observed in ectopic bone formation and those observed in transplantation into osteochondral defects. While the regeneration of articular cartilage in RUNX2-KO ECM presents intriguing results, the study lacked an exploration into underlying mechanisms, such as histological analyses at earlier time points.

Using RUNX2-KO ECM, we aimed at demonstrating the impact on cartilage remodeling and bone formation. This was performed ectopically but also in the rat osteochondral defect as a regenerative set-up of higher clinical relevance. We agree with the reviewer that additional experimental groups and time-points (not only earlier but also longer ones) would offer a better mechanistic understanding of the ECM contribution to the joint repair. However, as stated in our manuscript this is a proof-of-concept study that successfully demonstrated the influence of the cartilage ECM modification on the in vivo skeletal regeneration. A follow-up study would need to be performed to complement existing evidence and strengthen the relevance of our approach for cartilage repair.

Reviewer #2 (Public Review):

The manuscript submitted by Sujeethkumar et al. describes an alternative approach to skeletal tissue repair using extracellular matrix (ECM) deposited by genetically modified mesenchymal stromal/stem cells. Here, they generate a loss of function mutations in VEGF or RUNX2 in a BMP2-overexpressing MSC line and define the differences in the resulting tissue-engineered constructs following seeding onto a type I collagen matrix in vitro, and following lyophilization and subcutaneous and orthotopic implantation into mice and rats. Some strengths of this manuscript are the establishment of a platform by which modifications in cell-derived ECM can be evaluated both in vitro and in vivo, the demonstration that genetic modification of cells results in complexity of in vitro cell-derived ECM that elicits quantifiable results, and the admirable goal to improve endogenous cartilage repair. However, I recommend the authors clarify their conclusions and add more information regarding reproducibility, which was one limitation of primary-cell-derived ECMs.

We thank the reviewer for the positive evaluation of our work.

Overcoming the limitations of native/autologous/allogeneic ECMs such as complete decellularization and reduction of batch-to-batch variability was not specifically addressed in the data provided herein. For the maintenance of ECM organization and complexity following lyophilization, evidence of complete decellularization was not addressed, but could be easily evaluated using polarized light microscopy and quantification of human DNA for example in constructs pre and post-lyophilization.

We will clarify the experiments and characterization performed with lyophilized tissues versus those performed with decellularized ones. We will also provide evidence of DNA removal in our decellularized ECMs.

It would be ideal to see minimization of batch-to-batch variability using this approach, as mitigation of using a sole cell line is likely not sufficient (considering that the sole cell line-derived Matrigel does exhibit batch-to-batch and manufacturer-to-manufacturer variability). I recommend adding details regarding experimental design and outcomes not initially considered. Inter- and intra-experimental reproducibility was not adequately addressed. The size of in vitro-derived cartilage pellets was not quantified, and it is not clear that more than one independent 'differentiation' was performed from each gene-edited MSC line to generate in vitro replicates and constructs that were implanted in vivo.

We thank the Reviewer for the comment on variability/reproducibility concern. Using a cell line does confer higher robustness but indeed does not grant unlimited consistency of batch production. We will temper our claims in the discussion and mention the need to regularly re-characterize cell lines properties upon passages.

In our study, our grafts have been generated from various batches and tested in more than one experimental repeat. This will be further described in the revised version of our manuscript. We will also implement data on the size variability of generated tissues.

The use of descriptive language in describing conclusions may mislead the reader and should be modified accordingly throughout the manuscript. For example, although this reviewer agrees with the comparative statements made by the authors regarding parental and gene-edited MSC lines, non-quantifiable terms such as 'frank' 'superior' (example, line 242) are inappropriate and should rather be discussed in terms of significance. Another example is 'rich-collagenous matrix,' which was not substantiated by uniform immunostaining for type II collagen (line 189).

I have similar recommendations regarding conclusive statements from the rat implantation model, which was appropriately used for the purpose of evaluating the response of native skeletal cells to the different cell-derived ECMs. Interpretations of these results should be described with more accuracy. For example, increased TRAP staining does not indicate reduced active bone formation (line 237). Many would not conclude that GAGs were retained in the RUNX2-KO line graft subchondral region based on the histology. Quantification of % chondral regeneration using histology is not accurate as it is greatly influenced by the location in the defect from which the section was taken. Chondral regeneration is usually semi-quantified from gross observations of the cartilage surface immediately following excision. The statements regarding integration (example line 290) are not founded by histological evidence, which should show high magnification of the periphery of the graft adjacent to the native tissue.

We thank the Reviewer for the constructive suggestions. We will revise language accordingly throughout the manuscript.

Reviewer #3 (Public Review):

Summary:

In this study, the authors have started off using an immortalized human cell line and then gene-edited it to decrease the levels of VEGF1 (in order to influence vascularization), and the levels of Runx2 (to decrease chondro/osteogenesis). They first transplanted these cells with a collagen scaffold. The modified cells showed a decrease in vascularization when VEGF1 was decreased, and suggested an increase in cartilage formation.

In another study, the matrix generated by these cells was subsequently remodeled into a bone marrow organ. When RUNX2 was decreased, the cells did not mineralize in vitro, and their matrices expressed types I and II collagen but not type X collagen in vitro, in comparison with unedited cells. In vivo, the author claims that remodeling of the matrices into bone was somewhat inhibited. Lastly, they utilized matrices generated by RUNX2 edited cells to regenerate chondro-osteal defects. They suggest that the edited cells regenerated cartilage in comparison with unedited cells.

Strengths:

-The notion that inducing changes in the ECM by genetically editing the cells is a novel one, as it has long been thought that ECM composition influences cell activity.

-If successful, it may be possible to make off-the-shelf ECMS to carry out different types of tissue repair.

We thank the Reviewer for the critical evaluation of our work and the highlighted novelty of it.

Weaknesses:

-The authors have not generated histologically identifiable cartilage or bone in their transplants of the cells with a type I scaffold.

The chondrogenic differentiation of our MSOD-B line and their capacity of undergoing endochondral ossification has been robustly demonstrated in previous studies (Pigeot et al., Advanced Materials 2021 and Grigoryan et al., Science Translational Medicine 2022). In the present manuscript, we thus compare the chondrogenic capacity of newly established VEGF-KO and RUNX-KO lines to those of MSOD-B. We demonstrate by qualitative (Safranin-O staining, Collagen type 2 and Collagen type X immuno-stainings) and quantitative (glycosaminoglycans assay) assays that the generated tissues consist in cartilage tissue of similar quality than the MSOD-B. However, the safranin-O stainings were performed on lyophilized tissues, which can alter the staining quality/intensity. We will thus provide additional stainings of generated tissues pre-lyophilization.

On the contested formation of bone in vivo by our ECMs grafts, we have provided compelling qualitative evidence via Masson´s Trichrome stainings and quantification of mineralized volume by µCT. Both cortical bone and trabecular structures were identified ectopically. Those are standard evaluation methods in the field, we would be happy to receive additional suggestions by the Reviewer.

-In many cases, they did not generate histologically identifiable cartilage with their cell-free-edited scaffold. They did generate small amounts of bone but this is most likely due to BMPs that were synthesized by the cells and trapped in the matrix.

We now appreciate that the Reviewer agrees on the successful formation of bone induced by our engineered grafts. We however still respectfully disagree with the “small amount of bone” statement since our MSOD-B and MSOD-B VEGF KO cartilage grafts led to the full generation of a mature ectopic bone organ (that is, also composed of extensive marrow). This has been assessed qualitatively and quantitatively.

We agree with the Reviewer on the key role of BMP-2 in the remodeling process into bone and bone marrow, which we have extensively described in our previous publication (Pigeot et al., Advanced Materials 2021). We previously demonstrated that the low amount of BMP-2 (in the dozens of nanogram/tissue range) embedded in the matrix is not sufficient per se to induce ectopic endochondral ossification. It is the combined presence of GAGs in the matrix -thus cartilage- that allows the success of bone formation. Since we have already demonstrated in the present manuscript that the GAGs content is the same in MSOD-B and MSOD-B edited ECMs, we will provide additional data demonstrating the maintenance of BMP-2 content in all generated cartilage tissues.

-There is a great deal of missing detail in the manuscript.

We will provide additional information on the MSOD-B line and the overall methodology in our revised version.

-The in vivo study is underpowered, the results are not well documented pictorially, and are not convincing.

We will provide additional information and pictures related to our in vivo studies. We believe our group size supports our conclusions confirmed by statistical assessment.

-Given the fact that they have genetically modified cells, they could have done analyses of ECM components to determine what was different between the lines, both at the transcriptome and the protein level. Consequently, the study is purely descriptive and does not provide any mechanistic understanding of what mixture of matrix components and growth factors works best for cartilage or bone. But this presupposes that they actually induced the formation of bona fide cartilage, at least.

We thank the Reviewer for the suggestion. However, our study did not aim at understanding what ECM graft composition work best for cartilage nor bone regeneration respectively. Instead, we propose the exploitation of our cellular tools to interrogate the function of key ECM constituents and their impact in skeletal regeneration. We once more confirm that we generated lyophilized cartilage grafts which will be more evidently supported by histological assessment before lyophilization.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Chen and colleagues first compared the cartilage tissues collected from OA and HA patients using histology and immunostaining. Then, a genome-wide DNA methylation analysis was performed, which informed the changes of a novel gene, TNXB. IHC confirmed that TNXB has a lower expression level in HA cartilage than OA. Next, the authors demonstrated that TNXB levels were reduced in the HA animal model, and intraarticular injection of AAV carrying TNXB siRNA induced cartilage degradation and promoted chondrocyte apoptosis. Based on KEGG enrichment, histopathological analysis, and western blot, the authors also showed the relationship between TNXB and AKT phosphorylation. Lastly, AKT agonist, specifically SC79 in this study, was shown to partially rescue the changes of in vitro-cultured chondrocytes induced by Tnxb knock-down. Overall, this is an interesting study and provided sufficient data to support their conclusion.

Strengths:

(1) Both human and mouse samples were examined.

(2) The HA model was used.

(3) Genome-wide DNA methylation analysis was performed.

Weaknesses:

(1) In some experiments, the selection of the control groups was not ideal.

Thank you for comments. The reviewer raised the concerns about using human OA cartilage as control, instead of health cartilage. This is an important detail we didn’t describe in the previous version. We have added our explanation in revised Methods.

(2) More details on analyzing methods and information on replicates need to be included.

We greatly appreciate your careful review and helpful suggestions. We have added detailed information to our revised draft.

(3) Discussion can be improved by comparing findings to other relevant studies.

Thank the reviewer very much for the opportunity to improve our manuscript. We have improved discussions as reviewer suggested in Recommendation 13.

(4) The use of transgenic mice with conditional Tnxb depletion can further define the physiological roles of Tnxb.

Thanks for this valuable comment. We understand that conditional Tnxb-KO mice is much helpful for the study of biological roles of Tnxb, and it will be constructed and used in our future studies.

Recommendations For the Authors:

(1) Please add more information about HA such as incidence to highlight the importance of the study.

We greatly appreciate your careful review and helpful suggestions. We have provided more information about the importance of HA study in revised Introduction. Please see lines 90-93 and 103-112.

(2) Please justify the use of OA cartilage, instead of normal tissues, as the control.

Thanks for your suggestion. We certainly would have liked to use healthy cartilage as control, but we were extremely difficult to obtain enough control samples from healthy individuals. Despite the mechanistic and phenotypic differences between HA and OA, OA is often used as “disease” control to reveal the characteristics in HA 1,2. Thus, we measured cartilage degeneration and DNA methylation difference in HA and OA patients. We have provided the statement and evidence in revised manuscript. Please see lines 144-145.

(3) Please provide details of how to calculate the Cartilage wear area ratio in Figure 1D, and measure the positive staining area in Figure 1F.

We apologize for the issue you pointed out. Here, we provide detailed information for how positively stained areas are calculated. Specifically, in Figure 1D, we obtained the cartilage area ratio by calculating the ratio of blue cartilage staining area to the whole tissue area by using image J software. In Figure 1F, the area of positive staining was determined upon secondary antibody treatment and color development using DAB chromogen (brown stain). We then obtained the positive staining area ratio by calculating the ratio of positive staining area to the whole cartilage area by using image J software.

(4) Please label the location of hemorrhagic ferruginous deposits in Figure 1.

Thank you for your valuable suggestion. We have used black arrows to indicate hemorrhagic ferruginous deposits in revised Figure 1A.

(5) Please define the meaning of "n" in all figure legends, such as technical or biological replicates.

Thanks for your suggestion. We have defined the meaning of "n" in all figure legends in revised manuscript.

(6) In Figure 3, please increase the font size of B, D, F, H, and J. The same applies to other figures.

Thank you for your valuable suggestion. We have increased the font size of figures in our revised manuscript.

(7) Line 327, "(Figure 1, F and G)" should be Figure 2F, G.

Thanks for your reminding. We have corrected it in the revision. Please see lines 347.

(8) Reduced TNXB levels in human HA cartilage are one of the major findings in this study. Currently, only semi-quatative IHC was used to draw the conclusion. A second method, such as real-time PCR or western blot, is required.

Thanks for your suggestion. We feel very sorry that we did not have enough samples of human HA cartilages for qPCR and WB experiments, due to severe erosion of the HA cartilage. We have pointed out this limitation in revised drafts. Please see lines 445-448.

(9) Figure 3 shows that reduced Tnxb was accompanied by the increased Dnmt1. In addition, this study is about methylation. Have the authors tested the change of Dnmt1 levels when Tnxb was knocked down?

Thanks for your suggestion. According to the reviewer's suggestion, we have tested the expression of Dnmt1 in Tnxb-KD chondrocytes, and no significant alteration was observed. Please see the following Figure.

Author response image 1.

Figure Legend: Representative IHC staining of Dnmt1 in articular cartilage from Tnxb-KD HA mice. Corresponding quantification of the proportion of Dnmt1 positive regions. Red arrows indicate positive cells. Scale bar: 100 μm. Data were presented as means ± SD; n = 5 in each group. ns = no significance by unpaired Student’s t test.

(10) Also, is there a causal relationship between Tnxb levels and the distribution of methylation levels? Any related study was performed?

Following the valuable suggestion of the reviewer, we used two well-known DNA methyltransferase inhibitors (RG108 or 5-Aza-dc) 3 to examine whether DNA methylation regulates transcriptional expression of TNXB. We found that both inhibitors significantly up-regulated Tnxb mRNA level. We have added this result to the revised Supplementary Figure 4 and draft (lines 292-296 and 369-374).

(11) In Figure 6, what was the control of "AKT agnost" group?

Thank you for your suggestion. We feel sorry for our negligence and we have added the vehicle group as a control for AKT agonists in Figure 6 in our revised manuscript.

(12) Previous studies have reported the involvement of TNXB in TGF-β signaling. Have the authors examined the effect of TNXB on TGF-β signaling in chondrocytes?

Thank you for your suggestion. Here, we examined the expression of TGF-β signaling in Tnxb-KD chondrocyte and no significant changes were observed. We have discussed this result in revised draft (lines 475-479). We have added this result to the revised Supplementary Figure 7.

(13) Discussion can be improved. For example, have previous studies reported the association between TNXB and methylation in other cells/tissues? In addition to apoptosis, are there other potential mechanisms underlying the protective role of TNXB in chondrocytes?

Thank you for your valuable comments. Previous studies have shown the different DNA methylation of TNXB in whole blood from rheumatoid arthritis patients and in retinal pigment epithelium from patients with age-related macular degeneration 4,5. Herein, we were the first to report the association between DNA methylation of TNXB and HA cartilage degeneration. As for TNXB, there are limited public studies regarding physiological function of TNXB, among which mostly report the effect of TNXB on extracellular matrix organization 6,7. In our work, we found that TNXB regulated the phosphorylation of AKT. Since previous reports showed AKT controlled the expression of Mmp13 8, we thought that TNXB might regulated the chondrocyte extracellular matrix organization, in addition to its function on apoptosis. We have discussed these in revised manuscript (lines 462-464, and 495-501).

(14) The manuscript writing needs to be improved. Typos and grammar issues were noted.

Thanks. We have modified and polished our language and we hope the revised version could be acceptable for you.

Reviewer #2 (Public Review):

Summary:

This manuscript mainly studied the biological effect of tenascin XB (TNXB) on hemophilic arthropathy (HA) progression. Using bioinformatic and histopathological approaches, the authors identified the novel candidate gene TNXB for HA. Next, the authors showed that TNXB knockdown leads to chondrocyte apoptosis, matrix degeneration, and subchondral bone loss in vivo/vitro. Furthermore, AKT agonists promoted extracellular matrix synthesis and prevented apoptosis in TNXB knockdown chondrocytes.

Strengths:

In general, this study significantly advances our understanding of HA pathogenesis. The authors utilize comprehensive experimental strategies to demonstrate the role of TNXB in cartilage degeneration associated with HA. The results are clearly presented, and the conclusions appear appropriate.

Weaknesses:

Additional clarification is required regarding the gender of the F8-/- mouse in the study. Is the mouse male or female?

We feel sorry that we did not provide enough information about the gender of the F8-/- mouse in the previous draft. Here, we used male F8-/- mice as the study subjects for our experiments. Hemophilia A is predominantly seen in males because of the X chromosome linkage 9.

Recommendations For The Authors:

Some issues need to be addressed in the manuscript:

(1) During the progression of HA, in addition to cartilage degeneration, synovial hypertrophy and inflammation are also significant symptoms. How is the expression of TNXB in HA synovium?

Thank you for your valuable comments. According to the reviewer's suggestion, we tested the expression of TNXB in the synovium, and there was no statistically significant difference in the expression level of TNXB in the synovium (Supplementary Figure. 2) Please see lines 347-349.

(2) Lines 183-188. The methods of virus infection should be more detailed. What was the concentration of the AAVs injected? And how many doses were administrated?

Thank you for your suggestion. We have added an explanation of virus infection and injected doses in revised methods section (lines 205-206).

(3) Line 197-198. Could the author double-check the decalcification time for human cartilage samples? Is it for 3 months? Or for 3 weeks?

Thank you for your suggestion. We have reconfirmed the decalcification of human cartilage samples for 3 months.

(4) Line 343-344 "Above results suggest that TNXB might be protective against HA and its cartilage suppression is closely related to HA development." The conclusion is inappropriate, please revise it.

Thanks for your suggestion. We have revised this conclusion into “Above results suggest that the suppression of TNXB in cartilage promotes the HA development”. Please see lines 365-366.

(5) Line 326-327, the IHC staining for human samples is shown in Figure 2, not Figure 1. Please double check and revise it.

Thanks for your reminding. We feel sorry for our negligence and we have corrected it in the revision.

(6) For Figure 1B, it shows the MRI images of knee joints. However, the method section lacks details regarding the MRI imaging scan and analysis. Could the author include this information in the method section?

Thank you for your valuable comments. We have added the method of MRI imaging scan and analysis in revised Methods. Please see lines 154-163.

(7) In Figure 5, The statistical result of Bcl-2 is inconsistent with its Western blot band. Please check.

Thanks for your reminding. We have modified it in the revision.

(8) Please read through the text carefully to check for language problems. For example, in Line 68 "Our" not "our".

Thanks for your reminding. In revision, we have corrected it. Please see Line 68.

Reviewer #3 (Public Review):

Summary:

The manuscript by Dr. Chen et al. investigates the genes that are differentially methylated and associated with cartilage degeneration in hemophilia patients. The study demonstrates the functional mechanisms of the TNXB gene in chondrocytes and F8-/- mice. The authors first showed significant DNA methylation differences between hemophilic arthritis (HA) and osteoarthritis through genome-wide DNA methylation analysis. Subsequently, they showed a decreased expression of the differentially methylated TNXB gene in cartilage from HA patients and mice. By knocking down TNXB in vivo and in vitro, the results indicated that TNXB regulates extracellular matrix homeostasis and apoptosis by modulating p-AKT. The findings are novel and interesting, and the study presents valuable information in blood-induced arthritis research.

Strengths:

The authors adopted a comprehensive approach by combining genome-wide DNA methylation analysis, in vivo and in vitro experiments using human and mouse samples to illustrate the molecular mechanisms involved in HA progression, which is crucial for developing targeted therapeutic strategies. The study identifies Tenascin XB (TNXB) as a central mediator in cartilage matrix degradation. It provides mechanistic insights into how TNXB influences cartilage matrix degradation by regulating the activation of AKT. It opens avenues for future research and potential therapeutic interventions using AKT agonists for cartilage protection in hemophilic arthropathy. The conclusions drawn from the study are clear and directly tied to the findings.

Weaknesses:

(1) The study utilizes a small sample size (N=5 for both osteoarthritis and hemophilic arthropathy). A larger sample size would enhance the generalizability and statistical power of the findings.

Thank you for pointing out this deficiency. Indeed, our sample size is relatively small, although the overall sample size was sufficient for statistical analyses. And we have added this limitation in discussion in revised manuscript. Please see line 445-448. Considering the small sample size, we subsequently performed functional validation study for TNXB, one of the most significant genes, and demonstrated that TNXB exerted critical impacts on chondrocytes apoptosis in HA pathogenesis in vivo and in vitro.

(2) The use of an animal model (F8-/- mouse) to investigate the role of TNXB may not fully capture the complexity of human hemophilic arthropathy. Differences in the biology between species may affect the translatability of the findings to human patients.

Thank you for your valuable comments. We recognize that biological differences between species can affect the clinical translation of research findings. In our work, we sequenced human cartilage samples to obtain the differentially methylated gene-TNXB. Meanwhile, we demonstrated that protein expression of TNXB protein was significantly down-regulated in HA human cartilage and F8-/- transgenic mouse cartilage. The F8-/- transgenic mouse serves as a well-accepted model for the study of hemophilia, which is phenotypically similar to that of human patients suffering from the disease and spontaneously bleeds into the joints and soft tissues. Besides, this model mouse has been widely used in the study of hemophilia and hemophilic arthritis 9-11.

(3) The study primarily focuses on TNXB as a central mediator, but it might overlook other potentially relevant factors contributing to cartilage degradation in hemophilic arthropathy. A more holistic exploration of genetic and molecular factors could provide a broader understanding of the condition.

Thanks for your suggestion. Since our human sample size is relatively small, we should interpret differentially methylated genes cautiously. Therefore, we mainly focused on the most top significant gene TNXB for functional study. In our further study, we will expand the sample size to more comprehensively explore the molecular mechanisms of HA.

Recommendations For The Authors:

The following are my suggestions:

(1) Why do the authors choose to concentrate on the knee joint in the introduction when hemophilia, characterized by a deficiency in clotting factor F8, is recognized as a systemic disease?

Thank you for your valuable comments. Although hemophilia a systemic disease, approximately 80%-90% of bleeding episodes in patients with hemophilia occur within the musculoskeletal system, especially in the knee joint 12.

(2) While Figure 1 illustrates distinct expressions of Dnmt1 and Dnmt3a, only Dnmt1 results are presented in HA mice models in Figure 3. To address this, it is suggested that the expression of Dnmt3a be explored in animal models.

Thank you for your suggestion. According to the reviewer's suggestion, we examined the expression of Dnmt3a in mouse articular cartilage, and the expression level of Dnmt3a was significantly up-regulated in both the 4W and 8W model groups compared with the control group (Figure 3). Please see line 364.

(3) In Figure 3, the sample size for Dnmt1 is smaller than the other indicators; therefore, supplementing the sample count is recommended.

Thanks for your reminding. We have corrected it in the revision.

(4) Regarding Figure 4G, a few apoptotic cells were observed in the AAV NC group. It is advised that this figure be reviewed for accuracy.

Thanks for your suggestion. In Figure 5D, the AAV-NC group is the case of needle-injected with AAV. Therefore, it is normal for apoptotic cells to appear in the cartilage layer.

(5) The authors concluded that TNXB plays a role in apoptosis and AKT signaling. Providing expression data for Caspase9 would be valuable to strengthen this assertion, as PI3K/AKT signaling directly influences its activation during apoptosis.

Thank you for your comments. We have examined the expression of Cleaved-Caspase9 protein, and found that knockdown of TNXB resulted in upregulation of Cleaved-Caspase9 protein expression, which was reversed by addition of SC79. This result has added in revised Figure 6 and manuscript. Please see line 414.

(6) Quantitative analysis of the differences between the two groups in Supplemental Figures is necessary.

Thank you for your suggestion. We have added the quantitative analysis of the differences between the two groups in Supplemental Figures.

(7) With three major isoforms (homologs) of AKT in mammals-AKT1, 2, and 3 - why did the authors specifically focus on AKT1?

Thank you for your comments. Based on the results of the KEGG enrichment analysis of differential methylated genes, we investigated the role of PI3K/AKT pathway in apoptosis of HA chondrocytes. AKT is universally acknowledged as a core factor in the PI3K/AKT pathway that plays critical roles in various cellular activities such as cell proliferation, cell differentiation, cell apoptosis, metabolism and so on 13,14, More notably, several studies demonstrated that in AKT family, Akt1 primarily was involved in regulation of chondrocyte survival and proteoglycan synthesis 15. Therefore, we detected phosphorylation of AKT1 in HA cartilages and TNXB-KD chondrocytes, and found that TNXB regulation chondrocytes ECM and apoptosis by AKT1. Reference:

(1) Cooke, E.J., Zhou, J.Y., Wyseure, T., Joshi, S., Bhat, V., Durden, D.L., Mosnier, L.O., and von Drygalski, A. (2018). Vascular Permeability and Remodelling Coincide with Inflammatory and Reparative Processes after Joint Bleeding in Factor VIII-Deficient Mice. Thromb Haemost 118, 1036-1047. 10.1055/s-0038-1641755.

(2) Kleiboer, B., Layer, M.A., Cafuir, L.A., Cuker, A., Escobar, M., Eyster, M.E., Kraut, E., Leavitt, A.D., Lentz, S.R., Quon, D., et al. (2022). Postoperative bleeding complications in patients with hemophilia undergoing major orthopedic surgery: A prospective multicenter observational study. J Thromb Haemost 20, 857-865. 10.1111/jth.15654.

(3) Weiland, T., Weiller, M., Kunstle, G., and Wendel, A. (2009). Sensitization by 5-azacytidine toward death receptor-induced hepatic apoptosis. J Pharmacol Exp Ther 328, 107-115. 10.1124/jpet.108.143560.

(4) Anaparti, V., Agarwal, P., Smolik, I., Mookherjee, N., and El-Gabalawy, H. (2020). Whole Blood Targeted Bisulfite Sequencing and Differential Methylation in the C6ORF10 Gene of Patients with Rheumatoid Arthritis. J Rheumatol 47, 1614-1623. 10.3899/jrheum.190376.

(5) Porter, L.F., Saptarshi, N., Fang, Y., Rathi, S., den Hollander, A.I., de Jong, E.K., Clark, S.J., Bishop, P.N., Olsen, T.W., Liloglou, T., et al. (2019). Whole-genome methylation profiling of the retinal pigment epithelium of individuals with age-related macular degeneration reveals differential methylation of the SKI, GTF2H4, and TNXB genes. Clin Epigenetics 11, 6. 10.1186/s13148-019-0608-2.

(6) Mao, J.R., Taylor, G., Dean, W.B., Wagner, D.R., Afzal, V., Lotz, J.C., Rubin, E.M., and Bristow, J. (2002). Tenascin-X deficiency mimics Ehlers-Danlos syndrome in mice through alteration of collagen deposition. Nat Genet 30, 421-425. 10.1038/ng850.

(7) Zhang, K., Wang, X., Zeng, L.T., Yang, X., Cheng, X.F., Tian, H.J., Chen, C., Sun, X.J., Zhao, C.Q., Ma, H., and Zhao, J. (2023). Circular RNA PDK1 targets miR-4731-5p to enhance TNXB expression in ligamentum flavum hypertrophy. FASEB J 37, e22877. 10.1096/fj.202200022RR.

(8) Guo, H., Yin, W., Zou, Z., Zhang, C., Sun, M., Min, L., Yang, L., and Kong, L. (2021). Quercitrin alleviates cartilage extracellular matrix degradation and delays ACLT rat osteoarthritis development: An in vivo and in vitro study. J Adv Res 28, 255-267. 10.1016/j.jare.2020.06.020.

(9) Weitzmann, M.N., Roser-Page, S., Vikulina, T., Weiss, D., Hao, L., Baldwin, W.H., Yu, K., Del Mazo Arbona, N., McGee-Lawrence, M.E., Meeks, S.L., and Kempton, C.L. (2019). Reduced bone formation in males and increased bone resorption in females drive bone loss in hemophilia A mice. Blood Adv 3, 288-300. 10.1182/bloodadvances.2018027557.

(10) Haxaire, C., Hakobyan, N., Pannellini, T., Carballo, C., McIlwain, D., Mak, T.W., Rodeo, S., Acharya, S., Li, D., Szymonifka, J., et al. (2018). Blood-induced bone loss in murine hemophilic arthropathy is prevented by blocking the iRhom2/ADAM17/TNF-alpha pathway. Blood 132, 1064-1074. 10.1182/blood-2017-12-820571.

(11) Vols, K.K., Kjelgaard-Hansen, M., Ley, C.D., Hansen, A.K., and Petersen, M. (2019). Bleed volume of experimental knee haemarthrosis correlates with the subsequent degree of haemophilic arthropathy. Haemophilia 25, 324-333. 10.1111/hae.13672.

(12) Lobet, S., Peerlinck, K., Hermans, C., Van Damme, A., Staes, F., and Deschamps, K. (2020). Acquired multi-segment foot kinematics in haemophilic children, adolescents and young adults with or without haemophilic ankle arthropathy. Haemophilia 26, 701-710. 10.1111/hae.14076.

(13) Garcia, D., and Shaw, R.J. (2017). AMPK: Mechanisms of Cellular Energy Sensing and Restoration of Metabolic Balance. Mol Cell 66, 789-800. 10.1016/j.molcel.2017.05.032.

(14) Johnson, J., Chow, Z., Lee, E., Weiss, H.L., Evers, B.M., and Rychahou, P. (2021). Role of AMPK and Akt in triple negative breast cancer lung colonization. Neoplasia 23, 429-438. 10.1016/j.neo.2021.03.005.

(15) Rao, Z., Wang, S., and Wang, J. (2017). Peroxiredoxin 4 inhibits IL-1beta-induced chondrocyte apoptosis via PI3K/AKT signaling. Biomed Pharmacother 90, 414-420. 10.1016/j.biopha.2017.03.075.

Author response:

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

We thank the reviewers for their thorough review of and overall positive comments on our manuscript. We have revised the manuscript to address the one remaining concern raised by one of the reviewers. This is described below.

Fig.1B-C: To give a standard deviation from 2 data points has no statistical significance. In this case it would be better to define as range/difference of the 2 data points.

We have modified the legend for Figure 1 to now read, “The average of two experiments is plotted with the bars representing the range of each time point.”

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

In 'Systems analysis of miR-199a/b-5p and multiple miR-199a/b-5p targets during chondrogenesis', Patel et al. present a variety of analyses using different methodologies to investigate the importance of two miRNAs in regulating gene expression in a cellular model of cartilage development. They first re-analysed existing data to identify these miRNAs as one of the most dynamic across a chondrogenesis development time course. Next, they manipulated the expression of these miRNAs and showed that this affected the expression of various marker genes as expected. An RNA-seq experiment on these manipulations identified putative mRNA targets of the miRNAs which were also supported by bioinformatics predictions. These top hits were validated experimentally and, finally, a kinetic model was developed to demonstrate the relationship between the miRNAs and mRNAs studied throughout the paper.

I am convinced that the novel relationships reported here between miR-199a/b-5p and target genes FZD6, ITGA3, and CAV1 are likely to be genuine. It is important for researchers working on this system and related diseases to know all the miRNA/mRNA relationships but, as the authors have already published work studying the most dynamic miRNA (miR-140-5p) in this biological system I was not convinced that this study of the second miRNA in their list provided a conceptual advance on their previous work.

We believe this study is an enhancement on our previous work for two reasons, which have been alluded to in new text within the introduction. Firstly, our previous work used experimental and bioinformatic analysis to identify microRNAs with significant regulatory roles during chondrogenesis. This new manuscript additionally uses  a systems biology approaches to identify novel miRNA-mRNA interactions and capture these within an in silico model. Secondly, this work was initiated by the analysis of our previously generated data – using a novel tool we developed for this type of data (Bioconductor - TimiRGeN).  

I was also concerned with the lack of reporting of details of the manipulation experiments. The authors state that they have over-expressed miR-199a-5p (Figure 2A) and knocked down miR-199b-5p (Figure 2B) but they should have reported their proof that these experiments had worked as predicted, e.g. showing the qRT-PCR change in miRNA expression. Similarly, I was concerned that one miRNA was over-expressed while the other was knocked down - why did the authors not attempt to manipulate both miRNAs in both directions? Were they unable to achieve a significant change in miRNA expression or did these experiments not confirm the results reported in the manuscript?

We agree with the reviewer that some additional data were needed to demonstrate the effective regulation of miR-199-5p.  Hence, Supplementary Figure 1 is now included which provides validation of the effects of miR-199a-5p overexpression (Supplementary Figure 1A) and inhibition of miR-199a/b-5p (Supplementary Figure 1B). Within the main manuscript, Figure 2B has been amended to include the consequences of inhibition of miR-199a-5p, with 2C showing the consequences of miR-199b-5p inhibition. Further, we include new data with regards to miR-199a/b-5p inhibition on CAV1 (Figure 4A). 

I had a number of issues with the way in which some of the data was presented. Table 1 only reported whether a specific pathway was significant or not for a given differential expression analysis but this concealed the extent of this enrichment or the level of statistical significance reported. Could it be redrawn to more similarly match the format of Figure 3A? The various shades of grey in Figure 2 and Figure 4 made it impossible to discriminate between treatments and therefore identify whether these data supported the conclusions made in the text. It also appeared that the same results were reported in Figure 3B and 3C and, indeed, Figure 3B was not referred to in the main text. Perhaps this figure could be made more concise by removing one of these two sets of panels.

We agree with all points made here and have amended these within the manuscript. Figure 1A is now pathway enrichment plots from the TimiRGeN R Bioconductor package, and the table which previously showed the pathways enriched at each time point is now in the supplementary materials (supp. Table 1). Figure 2 and 4 now have color instead of shades of grey. Figure 3C has now been moved to supplementary materials (Supplementary Figure 2) and is referenced in the text. 

Overall, while I think that this is an interesting and valuable paper, I think its findings are relatively limited to those interested in the role of miRNAs in this specific biomedical context.

Reviewer #2 (Public review):

Summary:

This study represents an ambitious endeavor to comprehensively analyze the role of miR199a/b-5p and its networks in cartilage formation. By conducting experiments that go beyond in vitro MSC differentiation models, more robust conclusions can be achieved.

Strengths:

This research investigates the role of miR-199a/b-5p during chondrogenesis using bioinformatics and in vitro experimental systems. The significance of miRNAs in chondrogenesis and OA is crucial, warranting further research, and this study contributes novel insights.

Weaknesses:

While miR-140 and miR-455 are used as controls, these miRNAs have been demonstrated to be more relevant to Cartilage Homeostasis than chondrogenesis itself. Their deficiency has been genetically proven to induce Osteoarthritis in mice. Therefore, the results of this study should be considered in comparison with these existing findings.

We agree with the reviewers comments. miR-455-null mice develop normally but miR-140-null (or mutated) mice and humans do have skeletal abnormalities (e.g. Nat Med. 2019 Apr;25(4):583-590. doi: 10.1038/s41591-019-0353-2), indicating a role in chondrogenesis.  We have made an addition in the description to point towards the need to assess the roles miR-199a/b-5p may play during skeletogenesis and OA. We anticipate miR-199a/b-5p to be relevant in OA and have ongoing additional work for this – but this beyond the scope of this manuscript. 

Recommendations to Authors:

Reviewer #1 (Recommendations to authors):

Beyond the issues raised in the public review, I had a few minor recommendations that are largely designed to help improve the understanding of the manuscript as it is currently written.

(1) Please provide the statistical tests used to obtain p-values in the Figure 2 and 4 legends.

We have now added statistical test information to the figure legends of figures 2 and 4.

(2) It is stated on p. 9 that both miRNAs may share a functional repertoire because 25 and 341 genes are interested between their inhibition experiments. Please provide statistical support that this overlap is an enrichment over the null background in this experiment. Total DE genes – chi squared. Expected / Observed. 

A chi-squared test is now presented in the manuscript which shows that the number of significant genes which were found in common between miR-199a-5p knockdown and miR-199b-5p knockdown were significantly more than expected for day 0 or day 1 of the experiments. 

(3) The final sentence on p. 12 (beginning 'Size of the points reflect...') seemed out of place - is it part of a legend?

Thank you for pointing out this mistake - it was part of figure 3C and now is in the supplementary materials.

(4) A sentence on p. 14 reads that 'FZD6 and ITGA3 levels increased significantly' but this should read decreased, rather than increased. Quite an important typo!

Thank you for pointing this error out. It has been corrected.

(5) Theoretical transcripts are mentioned in the legend of Figure 5A but these were not present in the figure. Please include these or remove them from the legend.

This error has been removed form Figure 5A.

(6) On p 20, the references 22 and 27 should I think be moved to earlier in the sentence (after 'miR-199a-5p-FZD6 has been predicted previously'). Currently, it reads as if these references support your luciferase assays which you claim are the first evidence for this target relationship.

We agree with this change and have corrected the manuscript.

(7) The reference to Figure 5D on p. 20 should be a reference to Figure 5C.

Thank you for pointing this error out – this has been corrected.

Reviewer #2 (Recommendations to authors):

(1) The paper is based on the importance of miR-140 and miR-455 as miRNAs in chondrogenesis, citing only Barter, M. J. et al. Stem Cells 33, (2015). Considering the scope and results of this study, this citation is insufficient.

We agree with this reviewers comments. For many year miR-140 and miR-455 have been experimented on and their importance in OA research has become apparent. We included additional references within the introduction to address this.

(2) Analyzing chondrogenesis solely through differentiation experiments from MSCs is inadequate. It is essential to perform experiments involving the network within normal cartilage tissue and/or the generation of knockout mice to understand the precise role of miR199a/b-5p in chondrogenesis.

We have added an additional paragraph in the discussion to state this, and do believe it is highly important that miR-199a/b-5p be tested in OA samples – however this would be beyond the intended scope of this article.

(3) In light of the above points, it is imperative to investigate the role of miR-199a/b-5p beyond the in vitro differentiation model from MSCs, encompassing mouse OA models or human disease samples.

In tangent with the previous address, we agree with the pretense and believe additional experiments should be performed to gain more insight to the mechanism of how miR-199a/b-5p regulate OA. But development of a new mouse line to investigate this is not in the scope of this manuscript.

Author response:

Reviewer #1 (Public Review):

Summary:

In this study the authors use an elegant set of single-molecule experiments to assess the transcriptional and post-transcriptional regulation of RecB. The question stems from a previous observation from the same lab, that RecB protein levels are low and not induced under DNA damage. The authors first show that recB transcript levels are low and have a short half-life. They further show that RecB levels are likely regulated via translational control. They provide evidence for low noise in RecB protein levels across cells and show that the translation of the mRNA increases under double-strand break conditions. Authors identify Hfq binding sites in the recbcd [recBCD] operon and show that Hfq regulates the levels of RecB protein without changing the mRNA levels. They suggest that RecB translation is directly controlled by Hfq binding to mRNA, as mutating one of the binding sites has a direct effect on RecB protein levels.

Strengths:

The implication of Hfq in regulation of RecB translation is important and suggests mechanisms of cellular response to DNA damage that are beyond the canonically studied mechanisms (such as transcriptional regulation by LexA). Data are clearly presented and the writing is direct and easy to follow. Overall, the study is well-designed and provides novel insights into the regulation of RecB, that is part of the complex required to process break ends.

Weaknesses:

Some key findings need additional support/ clarifications to strengthen the conclusions. These are suggested to the authors.

Reviewer #2 (Public Review):

Summary:

The authors carry out a careful and rigorous quantitative analysis of RecB transcript and protein levels at baseline and in response to DNA damage. Using single-molecule FISH and Halo-tagging in order to achieve sensitive measurements, they provide evidence that enhanced RecB protein levels in response to DNA damage are achieved through a post-transcriptional mechanism mediated by the La-like RNA binding protein, Hhq1 [Sm-like RNA binding protein, Hfq]. In terms of biological relevance, the authors suggest that this mechanism provides a way to control the optimum level of RecB expression as both deletion and over-expression are deleterious. In addition, the proposed mechanism provides a new framework for understanding how transcriptional noise can be suppressed at the protein level.

Strengths:

Strengths of the manuscript include the rigorous approaches and orthogonal evidence to support the core conclusions, for example, the evidence that altering either Hhq1 [Hfq] or its recognition sequence on the RNA similarly enhance the protein to RNA ratio of RecB. The writing is clear and the experiments are well-controlled. The modeling approaches provide essential context to interpret the data, particularly given the small numbers of molecules per cell. The interpretations are careful and well supported.

Weaknesses:

The authors make a compelling case for the biological need to exquisitely control RecB levels, which they suggest is achieved by the pathway they have uncovered and described in this work. However, this conclusion is largely inferred as the authors only investigate the effect on cell survival in response to (high levels of) DNA damage and in response to two perturbations - genetic knock-out or over-expression, both of which are likely more dramatic than the range of expression levels observed in unstimulated and DNA damage conditions.

In the discussion, we proposed that the post-transcriptional regulation of recB that we have uncovered could be involved in keeping RecB levels within an optimal range. We agree that testing the phenotypic impact of small changes in RecB levels would add additional strength to this suggestion. However, this is experimentally very challenging because of the low copy number of RecB molecules, which makes it difficult to slightly alter RecB levels in a controlled and homogeneous (across cells) manner. Developing the synthetic biology tools necessary for such an experiment is beyond the scope of this article. In the manuscript, we will clarify the limits of our interpretation of the role of the uncovered regulation.

Reviewer #3 (Public Review):

Summary:

The work by Kalita et al. reports regulation of RecB expression by Hfq protein in E.coli cell. RecBCD is an essential complex for DNA repair and chromosome maintenance. The expression level needs to be regulated at low level under regular growth conditions but upregulated upon DNA damage. Through quantitative imaging, the authors demonstrate that recB mRNAs and proteins are expressed at low level under regular conditions. While the mRNA copy number demonstrates high noise level due to stochastic gene expression, the protein level is maintained at a lower noise level compared to expected value. Upon DNA damage, the authors claim that the recB mRNA level is not significantly affected, but RecB protein level increases due to a higher translation efficiency. [Upon DNA damage, the authors claim that the recB mRNA concentration is decreased, however RecB protein level is compensated by higher translation efficiency]. Through analyzing CLASH data on Hfq, they identified two Hfq binding sites on RecB polycistronic mRNA, one of which is localized at the ribosome binding site (RBS). Through measuring RecB mRNA and protein level in the ∆hfq cell, the authors conclude that binding of Hfq to the RBS region of recB mRNA suppresses translation of recB mRNA. This conclusion is further supported by the same measurement in the presence of Hfq sequestrator, the sRNA ChiX, and the deletion of the Hfq binding region on the mRNA.

Strengths:

(1) The manuscript is well-written and easy to understand.

(2) While there are reported cases of Hfq regulating translation of bound mRNAs, its effect on reducing translation noise is relatively new.

(3) The imaging and analysis are carefully performed with necessary controls.

Weaknesses:

The major weaknesses include a lack of mechanistic depth, and part of the conclusions are not fully supported by the data.

(1) Mechanistically, it is still unclear why upon DNA damage, translation level of recB mRNA increases, which makes the story less complete. The authors mention in the Discussion that a moderate (30%) decrease in Hfq protein was observed in previous study, which may explain the loss of translation repression on recB. However, given that this mRNA exists in very low copy number (a few per cell) and that Hfq copy number is on the order of a few hundred to a few thousand, it's unclear how 30% decrease in the protein level should resides a significant change in its regulation of recB mRNA.

While Hfq is a highly abundant protein, it has many mRNA and sRNA targets, some of which are also present in large amounts (DOI: 10.1046/j.1365-2958.2003.03734.x). As recently shown, the competition among the targets over Hfq proteins results in unequal (across various targets) outcomes, where the targets with higher Hfq affinity have an advantage over the ones with less efficient binding (DOI: 10.1016/j.celrep.2020.02.016). In line with these findings, we reason that upon DNA damage, a moderate decrease in the Hfq protein abundance (30%) can lead to a similar competition among Hfq targets where high-affinity targets outcompete low- affinity ones as well as low-abundant ones (such as recB mRNAs). Therefore, we hypothesise that the regulation of low abundant targets of Hfq by moderate perturbations of Hfq protein level is a potential explanation for the change in RecB translation that we have observed. We will expand this part of the discussion to explain our reasoning in a more explicit and coherent way.

(2) Based on the experiment and the model, Hfq regulates translation of recB gene through binding to the RBS of the upstream ptrA gene through translation coupling. In this case, one would expect that the behavior of ptrA gene expression and its response to Hfq regulation would be quite similar to recB. Performing the same measurement on ptrA gene expression in the presence and absence of Hfq would strengthen the conclusion and model

Indeed, based on our model, we expect PtrA expression to be regulated by Hfq in a similar manner to RecB. However, the product encoded by the ptrA gene, Protease III, (i) has been poorly characterised; (ii) unlike RecB, is located in the periplasm (DOI: 10.1128/jb.149.3.1027-1033.1982); and (iii) is not involved in any DNA repair pathway. Therefore, analysing PtrA expression would take us away from the key questions of our study.

(3) The authors agree that they cannot exclude the possibility of sRNA being involved in the translation regulation. However, this can be tested by performing the imaging experiments in the presence of Hfq proximal face mutations, which largely disrupt binding of sRNAs.

(4) The data on construct with a long region of Hfq binding site on recB mRNA deleted is less convincing. There is no control to show that removing this sequence region itself has no effect on translation, and the effect is solely due to the lack of Hfq binding. A better experiment would be using a Hfq distal face mutant that is deficient in binding to the ARN motifs.

We thank the referee for these suggestions. We have performed the requested experiments, and the quantification of RecB abundance in the presence of Hfq proteins mutated in the proximal and distal face will be added to the revised version of the manuscript.

(5) Ln 249-251: The authors claim that the stability of recB mRNA is not changed in ∆hfq simply based on the steady-state mRNA level. To claim so, the lifetime needs to be measured in the absence of Hfq.

We agree that this statement is not fully supported by our data and will address this issue in the revised version.

(6) What's the labeling efficiency of Halo-tag? If not 100% labeled, is it considered in the protein number quantification? Is the protein copy number quantification through imaging calibrated by an independent method? Does Halo tag affect the protein translation or degradation?

Our previous study (DOI: 10.1038/s41598-019-44278-0) described a detailed characterisation of the HaloTag labelling technique for quantifying low-copy proteins in single E. coli cells.

In that study, we used RecB-HaloTag as an example of a low-copy number protein. We showed a complete quantitative agreement of RecB detection between two fully independent methods: HaloTag-based labelling with cell fixation and RecB-sfGFP combined with a microfluidic device that lowers protein diffusion in the bacterial cytoplasm. This second method has previously been validated for protein quantification (DOI: 10.1038/ncomms11641) and provides detection of 80-90% of the labelled protein. Additionally, in our protocol, immediate chemical fixation of cells after the labelling and quick washing steps ensure that new, unlabelled RecB proteins are not produced. We, therefore, conclude that our approach to RecB detection is highly reliable and sufficient for comparing RecB production in different conditions and mutants.

The RecB-HaloTag construct has been designed for minimal impact on RecB production and function. The HaloTag is translationally fused to RecB in a loop positioned after the serine present at position 47 where it is unlikely to interfere with (i) the formation of RecBCD complex (based on RecBCD structure, DOI: 10.1038/nature02988), (ii) the initiation of translation (as it is far away from the 5’UTR and the beginning of the open reading frame) and (iii) conventional C-terminal-associated mechanisms of protein degradation (DOI: 10.15252/msb.20199208). In our manuscript, we showed that the RecB-HaloTag degradation rate is similar to the dilution rate due to bacterial growth. This is in line with a recent study on unlabelled proteins, which shows that RecB’s lifetime is set by the cellular growth rate (https://doi.org/10.1101/2022.08.01.502339) and indicates that the HaloTag fusion is not affecting RecB stability.

Furthermore, we have demonstrated (DOI: 10.1038/s41598-019-44278-0) that (i) bacterial growth is not affected by replacing the native RecB with RecB-HaloTag, (ii) RecB-HaloTag is fully functional upon DNA damage, and (iii) no proteolytic processing of the RecB-HaloTag is detected by Western blot.

These results suggest that RecB expression and functionality are unlikely to be affected by the translational HaloTag insertion at Ser-47 in RecB. In the revised version of the manuscript, we will add information about the construct and discuss the reliability of the quantification.

(7) Upper panel of Fig S8a is redundant as in Fig 5B. Seems that Fig S8d is not described in the text.

Indeed, the data in the upper panel in Fig S8a was repeated (from Fig 5B) for visual purposes to facilitate comparison with the panel below. We will modify the figure legend to indicate this repetition clearly.

In Fig S8d, we confirmed the functionality of the Hfq protein expressed from the pQE-Hfq plasmid in our experimental conditions, which was not described in the text. We will include this clarification in the updated manuscript.

Author response:

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

We would like to first thank the Editor as well as the three reviewers for their enthusiasm and conducting another careful evaluation of our manuscript. We appreciate their thoughtful and constructive comments and suggestions. Some concerns regarding experimental design, data analysis, and over-interpretation of our findings still remains unresolved after the initial revision. Here we endeavored to address these remaining concerns through further refinement of our writing, and inclusion of these concerns in the discussion session. We hope our response can better explain the rationale of our experimental design and data interpretation. In addition, we also acknowledge the limitations of our present study, so that it will benefit future investigations into this topic. Our detail responses are provided below.

Reviewer #1 (Public Review):

This study examines whether the human brain uses a hexagonal grid-like representation to navigate in a non-spatial space constructed by competence and trustworthiness. To test this, the authors asked human participants to learn the levels of competence and trustworthiness for six faces by associating them with specific lengths of bar graphs that indicate their levels in each trait. After learning, participants were asked to extrapolate the location from the partially observed morphing bar graphs. Using fMRI, the authors identified brain areas where activity is modulated by the angles of morphing trajectories in six-fold symmetry. The strength of this paper lies in the question it attempts to address. Specifically, the question of whether and how the human brain uses grid-like representations not only for spatial navigation but also for navigating abstract concepts, such as social space, and guiding everyday decision-making. This question is of emerging importance.

I acknowledge the authors' efforts to address the comments received. However, my concerns persist:

Thanks very much again for the re-evaluation and comments. Please find our revision plans to each comment below.

(1) The authors contend that shorter reaction times correlated with increased distances between individuals in social space imply that participants construct and utilize two-dimensional representations. This method is adapted from a previous study by Park et al. Yet, there is a fundamental distinction between the two studies. In the prior work, participants learned relationships between adjacent individuals, receiving feedback on their decisions, akin to learning spatial locations during navigation. This setup leads to two different predictions: If participants rely on memory to infer relationships, recalling more pairs would be necessary for distant individuals than for closer ones. Conversely, if participants can directly gauge distances using a cognitive map, they would estimate distances between far individuals as quickly as for closer ones. Consequently, as the authors suggest, reaction times ought to decrease with increasing decision value, which, in this context, corresponds to distances. However, the current study allowed participants to compare all possible pairs without restricting learning experiences, rendering the application of the same methodology for testing two-dimensional representations inappropriate. In this study, the results could be interpreted as participants not forming and utilizing two-dimensional representations.

We apologize for not being clear enough about our task design, we have made relevant changes in the methodology section in the manuscript to make it clearer. The reviewer’s concern is that participants learned about all the pairs in the comparison task which makes the distance effect invalid. We would like to clarify that during all the memory test tasks (the comparison task, the collect task and the recall task outside and inside scanner), participants never received feedback on whether their responses were correct or not. Therefore, the comparison task in our study is similar to the previous study by Park et al. (2021). Participants do not have access to correct responses for all possible pairs of comparison prior to or during this task, they would need to make inference based on memory retrieval.

(2) The confounding of visual features with the value of social decision-making complicates the interpretation of this study's results. It remains unclear whether the observed grid-like effects are due to visual features or are genuinely indicative of value-based decision-making, as argued by the authors. Contrary to the authors' argument, this issue was not present in the previous study (Constantinescu et al.). In that study, participants associated specific stimuli with the identities of hidden items, but these stimuli were not linked to decision-making values (i.e., no image was considered superior to another). The current study's paradigm is more akin to that of Bao et al., which the authors mention in the context of RSA analysis. Indeed, Bao et al. controlled the length of the bars specifically to address the problem highlighted here. Regrettably, in the current paradigm, this conflation remains inseparable.

We’d like to thank the reviewer for facilitating the discussion on the question of ‘social space’ vs. ‘sensory space’. The task in scanner did not require value-based decision making. It is akin to both the Bao et al. (2019) study and Constantinescu et al. (2016) study in a sense that all three tasks are trying to ask participants to imagine moving along a trajectory in an abstract, non-physical space and the trajectory is grounded in sensory cue. Participants were trained to associate the sensory cue with abstract (social/nonsocial) concepts. We think that the paradigm is a relatively faithful replication of the study by Constantinescu et al. Nonetheless, we agreed that a design similar to Bao et al. (2019) which controls for sensory confounds would be more ideal to address this concern, or adopting a value-based decision-making task in the scanner similar to that by Park et al. (2021), and we have included this limitation in the discussion section.

(3) While the authors have responded to comments in the public review, my concerns noted in the Recommendation section remain unaddressed. As indicated in my recommendations, there are aspects of the authors' methodology and results that I find difficult to comprehend. Resolving these issues is imperative to facilitate an appropriate review in subsequent stages.

Considering that the issues raised in the previous comments remain unresolved, I have retained my earlier comments below for review.

We apologize for not addressing the recommendations properly, please find detailed our response and plans for revision.

I have some comments. I hope that these can help.

(1) While the explanation of Fig.4A-C is lacking in both the main text and figure legend, I am not sure if I understand this finding correctly. Did the authors find the effects of hexagonal modulation in the medial temporal gyrus and lingual gyrus correlate with the individual differences in the extent to which their reaction times were associated with the distances between faces when choosing a better collaborator? If so, I am not sure what argument the authors try to draw from these findings. Do the authors argue that these brain areas show hexagonal modulation, which was not supported in the previous analysis (Fig.3)? What is the level of correlation between these behavioral measures and the grid consistency effects in the vmPFC and EC, where the authors found actual grid-like activity? How do the authors interpret this finding? More importantly, how does this finding associate with other findings and the argument of the study?

We apologize for not being clear enough in the manuscript and we will improve the clarity in our revision. This exploratory analysis reported in Figure 4 aims to use whole-brain analysis to examine: 1) if there is any correlation between the strength of grid-like representation of social value map and behavioral indicators of map-like representation; and 2) if there are any correlation between the strength of grid-like representation of this social value map and participants’ social trait.

To be more specific, for the behavioral indicator, we used the distance effect in the reaction time of the comparison task outside the scanner. We interpreted stronger distance effect as a behavioral index of having better internal map-like representation. We interpreted stronger grid consistency effect as a neural index of better representation of the 2D social space. Therefore, we’d like to see if there exists correlation between behavioral and neural indices of map-like representation.

To achieve this goal, behavioral indicators are entered as covariates in second-level analysis of the GLM testing grid consistency effect (GLM2). Figure3 showed results from GLM2 without the covariates. Figure4 showed results of clusters whose neural indices of map-like representation covaried with that from behavior and survived multiple-comparison correction. Indeed, in these regions, the grid consistency effect was not significant at group level (so not shown in Figure 3). We tried to interpret this finding in our discussion (line 374-289 for temporal lobe correlation, line 395-404 for precuneus correlation).

Finally, we would like to point out that including the covariates in GLM2 did not change results in Figure3, the clusters in Figure3 still survives correction. Meanwhile, these clusters in Figure 3 did not show correlation with behavioral indicators of map-like representation.

Author response image 1.

(2) There are no behavioral results provided. How accurately did participants perform each of the tasks? How are the effects of grid consistency associated with the level of accuracy in the map test?

Why did participants perform the recall task again outside the scanner?

We will endeavor to improve signposting the corresponding figures in the main text. For the behavioral results, we reported the stats in section “Participants construct social value map after associative learning of avatars and corresponding characteristics” in the main text, and the plots are shown in Figure 1. Particularly, figure 1F showed accuracy of tasks in training, as well as the recall task in the scanner. For the correlation, we did not find significant correlation between behavioural accuracy and grid consistency effect. We will make it clearer in the result section.

(3) The methods did not explain how the grid orientation was estimated and what the regressors were in GLM2. I don't think equations 2 and 3 are quite right.

For the grid orientation estimation method, we provided detailed description in the Supplementary methods 2.2.2. We will add links to this section in the main text.

Equation 2 and 3 describes how the parametric regressors entered into GLM2 were formed and provided prerequisites on calculation of grid orientations. Equation 2 was the results of directly applying the angle addition and subtraction theorems so they should be correct. We will try to make the rationale clearer in the supplementary text.

(4) With the increase in navigation distances, more grid cells would activate. Therefore, in theory, the activity in the entorhinal cortex should increase with the Euclidean distances, which has not been found here. I wonder if there was enough variability in the Euclidean distances that can be captured by neural correlates. This would require including the distributions of Euclidean distances according to their trajectory angles. Regarding how Fig.1E is generated, I don't understand what this heat map indicates. Additionally, it needs to be confirmed if the grid effects remain while controlling for the Euclidean distances of navigation trajectories.

We did not specifically control for the trajectory length, we only controlled for the distribution of trajectory to be uniform. We have included a figure of the distribution of Euclidean distances in Figure S9 and the distribution of trajectory direction in Figure S8.

Author response image 2.

As for Figure 1E, we aim to reproduce the findings from Figure 1F in Constantinescu et al. (2016) where they showed that participants progressively refined the locations of the outcomes through training. We divided the space into 15×15 subregions and computed the amount of time spent in each subregion and plotted Figure 1E. Brighter color in Figure 1E indicate greater amount of time spent in the corresponding subregion. Note that all these timing indices were computed as a percentage of the total time spent in the explore task in a given session. If participants were well-acquainted with the space and avatars, they would spend more time at the avatar (brighter color in avatar locations) in the review session compared to the learning session.

As for the effect of distances on grid-like representation, we did not include the distance as a parametric modulator in grid consistency effect GLM (GLM2) due to insufficient trials in each bin (6-8 trials). But there is side evidence that could potentially rule out this confound. In the distance representation analysis, we did not find distance representation in any of the clusters that have significant grid-like representation (regions in Figure 2).

Reviewer #2 (Public Review):

Summary:

In this work, Liang et al. investigate whether an abstract social space is neurally represented by a grid-like code. They trained participants to 'navigate' around a two-dimensional space of social agents characterized by the traits warmth and competence, then measured neural activity as participants imagined navigating through this space. The primary neural analysis consisted of three procedures: 1) identifying brain regions exhibiting the hexagonal modulation characteristic of a grid-like code, 2) estimating the orientation of each region's grid, and 3) testing whether the strength of the univariate neural signal increases when a participant is navigating in a direction aligned with the grid, compared to a direction that is misaligned with the grid. From these analyses, the authors find the clearest evidence of a grid-like code in the prefrontal cortex and weaker evidence in the entorhinal cortex.

Strengths:

The work demonstrates the existence of a grid-like neural code for a socially-relevant task, providing evidence that such coding schemes may be relevant for a variety of two-dimensional task spaces.

Weaknesses:

In the revised manuscript, the authors soften their claims about finding a grid code in the entorhinal cortex and provide additional caveats about limitations in their findings. It seems that the authors and reviewers are in agreement about the following weaknesses, which were part of my original review: Claims about a grid code in the entorhinal cortex are not well-supported by the analyses presented. The whole-brain analysis does not suggest that the entorhinal cortex exhibits hexagonal modulation; the strength of the entorhinal BOLD signal does not track the putative alignment of the grid code there; multivariate analyses do not reveal any evidence of a grid-like representational geometry.

In the authors' response to reviews, they provide additional clarification about their exploratory analyses examining whether behavior (i.e., reaction times) and individual difference measures (i.e., social anxiety and avoidance) can be predicted by the hexagonal modulation strength in some region X, conditional on region X having a similar estimated grid alignment with some other region Y. My guess is that readers would find it useful if some of this language were included in the main text, especially with regard to an explanation regarding the rationale for these exploratory studies.

Thank you very much again for your careful re-evaluation and suggestions. We have tried to improve our writing and incorporate the suggestions in the new revision.

Reviewer #3 (Public Review):

Liang and colleagues set out to test whether the human brain uses distance and grid-like codes in social knowledge using a design where participants had to navigate in a two-dimensional social space based on competence and warmth during an fMRI scan. They showed that participants were able to navigate the social space and found distance-based codes as well as grid-like codes in various brain regions, and the grid-like code correlated with behavior (reaction times).

On the whole, the experiment is designed appropriately for testing for distant-based and grid-like codes, and is relatively well powered for this type of study, with a large amount of behavioral training per participant. They revealed that a number of brain regions correlated positively or negatively with distance in the social space, and found grid-like codes in the frontal polar cortex and posterior medial entorhinal cortex, the latter in line with prior findings on grid-like activity in entorhinal cortex. The current paper seems quite similar conceptually and in design to previous work, most notably Park et al., 2021, Nature Neuroscience.

(1) The authors claim that this study provides evidence that humans use a spatial / grid code for abstract knowledge like social knowledge.

This data does specifically not add anything new to this argument. As with almost all studies that test for a grid code in a similar "conceptual" space (not only the current study), the problem is that, when the space is not a uniform, square/circular space, and 2-dimensional then there is no reason the code will be perfectly grid like, i.e., show six-fold symmetry. In real world scenarios of social space (as well as navigation, semantic concepts), it must be higher dimensional - or at least more than two dimensional. It is unclear if this generalizes to larger spaces where not all part of the space is relevant. Modelling work from Tim Behrens' lab (e.g., Whittington et al., 2020) and Bradley Love's lab (e.g., Mok & Love, 2019) have shown/argued this to be the case. In experimental work, like in mazes from the Mosers' labs (e.g., Derdikman et al., 2009), or trapezoid environments from the O'Keefe lab (Krupic et al., 2015), there are distortions in mEC cells, and would not pass as grid cells in terms of the six-fold symmetry criterion.

The authors briefly discuss the limitations of this at the very end but do not really say how this speaks to the goal of their study and the claim that social space or knowledge is organized as a grid code and if it is in fact used in the brain in their study and beyond. This issue deserves to be discussed in more depth, possibly referring to prior work that addressed this, and raise the issue for future work to address the problem - or if the authors think it is a problem at all.

Thanks very much again for your careful re-evaluation and comments. We have tried to incorporate some of the suggested papers into our discussion. In summary, we agree that there is more to six-fold symmetric code that can be utilized to represent “conceptual space”. We think that the next step for a stronger claim would be to find the representation of more spontaneous non-spatial maps.

References

Bao, X., Gjorgieva, E., Shanahan, L. K., Howard, J. D., Kahnt, T., & Gottfried, J. A. (2019). Grid-like Neural Representations Support Olfactory Navigation of a Two-Dimensional Odor Space. Neuron, 102(5), 1066-1075 e1065. https://doi.org/10.1016/j.neuron.2019.03.034

Constantinescu, A. O., O'Reilly, J. X., & Behrens, T. E. J. (2016). Organizing conceptual knowledge in humans with a gridlike code. Science, 352(6292), 1464-1468. https://doi.org/10.1126/science.aaf0941

Park, S. A., Miller, D. S., & Boorman, E. D. (2021). Inferences on a multidimensional social hierarchy use a grid-like code. Nat Neurosci, 24(9), 1292-1301. https://doi.org/10.1038/s41593-02100916-3

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Although this manuscript contains a potentially interesting piece of work that delineates a mechanism of IQCH that associates with spermatogenesis, this reviewer feels that a number of issues require clarification and re-evaluation for a better understanding of the role of IQCH in spermatogenesis. With the shortage of logics and supporting data, causal relationships are still not clear among IQCH, CaM, and HNRPAB. The most serious point in this manuscript could be that the authors try to generalize their interpretations with too simplified model from limited pieces of their data. The way the data and the logic are presented needs to be largely revised, and several interpretations should be supported by direct evidence.

Response: Thank you for the reviewer’s comment. IQCH is a calmodulin-binding protein, and the binding of IQCH and CaM was confirmed by LC-MS/MS analysis and co-IP assay using sperm lysate. We thus speculated that if the interaction of IQCH and CaM might be a prerequisite for IQCH function. To prove that speculation, we took HNRPAB as an example. We knocked down IQCH in cultured cells, and a decrease in the expression of HNRPAB was observed. Similarly, when we knocked down CaM in cultured cells, and a decrease in the expression of HNRPAB was also detected. However, these results cannot exclude that IQCH or CaM could regulate HNRPAB expression alone. To investigate that if IQCH or CaM could regulate HNRPAB expression alone, we overexpressed IQCH in cells that knocked down CaM, while the expression of HNRPAB cannot be rescued, suggesting that IQCH cannot regulate HNRPAB expression when CaM is reduced. In consistent, we overexpressed CaM in cells that knocked down IQCH, while the expression of HNRPAB cannot be rescued, suggesting that CaM cannot regulate HNRPAB expression when IQCH is reduced. Thus, IQCH or CaM cannot regulate HNRPAB expression alone. Moreover, we deleted the IQ motif of IQCH, which is required for binding to CaM. The co-IP results showed that the interaction of IQCH and CaM was disrupted when deleting the IQ motif of IQCH, and the expression of HNRPAB was decreased. Therefore, we suggested that the interaction of IQCH and CaM might be required for IQCH regulating HNRPAB. In future studies, we will further investigate the relationships among IQCH, CaM, and HNRPAB.

Reviewer #3 (Public Review):

(1) More background details are needed regarding the proteins involved, in particular IQ proteins and calmodulin. The authors state that IQ proteins are not well-represented in the literature, but do not state how many IQ proteins are encoded in the genome. They also do not provide specifics regarding which calmodulins are involved, since there are at least 5 family members in mice and humans. This information could help provide more granular details about the mechanism to the reader and help place the findings in context.

Response: Thanks to reviewer’s suggestion. We have provided additional background information regarding IQ-containing protein family members in humans and mice, as well as other IQ-containing proteins implicated in male fertility, in the Introduction section. Furthermore, we have supplemented the Introduction with background information concerning the association between CaM and male infertility.

(2) The mouse fertility tests could be improved with more depth and rigor. There was no data regarding copulatory plug rate; data was unclear regarding how many WT females were used for the male breeding tests and how many litters were generated; the general methodology used for the breeding tests in the Methods section was not very explicitly or clearly described; the sample size of n=3 for the male breeding tests is rather small for that type of assay; and, given that ICHQ appears to be expressed in testicular interstitial cells (Fig. S10) and somewhat in other organs (Fig. S2), another important parameter of male fertility that should be addressed is reproductive hormone levels (e.g., LH, FSH, and testosterone). While normal epididymal size in Fig. S3 suggests that hormone (testosterone) levels are normal, epididymal size and/or weight were not rigorously quantified.

Response: Thanks to reviewer’s comment. We have provided the data regarding copulatory plug rate and the average number of litters for breeding tests in revised Figure 3—figure supplement 2. The methodology used for the breeding tests has been revised to be more detailed and explicit in the revised Method section. Moreover, we have increased the sample size for male breeding tests to n=6. We measured the serum levels of FSH, LH, and Testosterone in the WT (9.3±1.9 ng/ml, 0.93±0.15 ng/ml, and 0.2±0.03 ng/ml) and Iqch KO mice (12±2 ng/ml, 1.17±0.2 ng/ml, and 0.2±0.04 ng/ml). There was no significant difference observed in the serum levels of reproductive hormones between WT and Iqch KO mice; therefore, we did not include the data in the study. Furthermore, we have added quantitative data on epididymal size in the revised Figure 3—figure supplement 2.

(3) The Western blots in Figure 6 should be rigorously quantified from multiple independent experiments so that there is stronger evidence supporting claims based on those assays.

Response: We appreciate the reviewer's comment. As suggested, we have added quantified data in Figure 6—figure supplement 2 from the results of Western blotting in Figure 6.

(4) Some of the mouse testis images could be improved. For example, the PNA and PLCz images in Figure S7 are difficult to interpret in that the tubules do not appear to be stage-matched, and since the authors claimed that testicular histology is unaffected in knockout testes, it should be feasible to stage-match control and knockout samples. Also, the anti-ICHQ and CaM immunofluorescence in Figure S10 would benefit from some cell-type-specific co-stains to more rigorously define their expression patterns, and they should also be stage-matched.

Response: Thanks to reviewer’s suggestions. We have included immunofluorescence images of anti-PLCz, anti-PNA and anti-IQCH and CaM during spermatogenesis development.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) There are multiple grammatical errors and statements drawn beyond the results. The entire manuscript would benefit from professional editing.

Response: We are sorry for the grammatical errors. We have enlisted professional editing services to refine our manuscript.

(2) Line 40, "Firstly" is not appropriate here.

Response: Thanks to reviewer’s comment. The word "Firstly" has been removed from the revised manuscript.

(3) Line 44, "processes".

Response: Thanks to reviewer’s suggestion. We have changed “process” in to “processes” on line 45.

(4) "spermatocytogenesis (mitosis)" is incorrect.

Response: Thanks to reviewer’s comment. We have changed “spermatocytogenesis (mitosis)” in to “mitosis” on line 47.

(5) Ca and Ca2+ are both used in line 67 - 77. Be consistent.

Response: We appreciate the reviewer's detailed checks. We have maintained consistency by revising instances of "Ca" to "Ca2+" in revised manuscript.

(6) Line 238 to 240, "To elucidate the molecular mechanism by which IQCH regulates male fertility, we performed liquid chromatography tandem mass spectrometry (LC-MS/MS) analysis using mouse sperm lysates and detected 288 interactors of IQCH (Data S1)."It is not clear how LC-MS/MS using mouse sperm lysates could detect "288 interactors of IQCH"? A co-IP experiment for IQCH using sperm lysates prior to LC-MS/MS is needed to detect "interactors of IQCH". However, in the Methods section, consistent with the main text, proteomic quantification was conducted for protein extract from sperm. Figure legend for Fig. 5 did not explain this, either.Thus, it is unable to evaluate Figure 5.

Response: We sincerely apologize for the oversight. Following reviewer’s suggestions, we have supplemented the method details of LC-MS/MS experiment in the Methods section of revised manuscript. Additionally, we conducted a co-IP experiment for IQCH using sperm lysates prior to LC-MS/MS and we did not include the corresponding figure in the manuscript. The results are as follows:

Author response image 1.

The results of a co-IP experiment for IQCH using sperm lysates from WT mice.

(7) Line 246, "... key proteins that might be activated by IQCH". What does "activated" here refer to? Should it be "upregulated"?

Response: We are sorry to our inexact statement. Instead, "upregulated" would better convey the intended meaning. According to reviewer’s suggestions, we have modified "activated" into "upregulated".

(8) Line 252 to 254, "the cross-analysis revealed that 76 proteins were shared between the IQCH-bound proteins and the IQCH-activated proteins (Fig. 5E), implicating this subset of genes as direct targets." This is a confusing statement. Is the author trying to say, IQCH-bound proteins have upregulated expression, suggesting that IQCH enhances their expression?

Response: We appreciate the reviewer's comment regarding the clarity of the statement in Line 252 to 254 of the manuscript. We have modified this sentence into “Importantly, cross-analysis revealed that 76 proteins were shared between the IQCH-bound proteins and the downregulated proteins in Iqch KO mice (Figure 5E), suggesting that IQCH might regulate their expression by the interaction.”

(9) Line 260 to 261, "SYNCRIP, HNRNPK, FUS, EWSR1, ANXA7, SLC25A4, and HNRPAB ... the loss of which showed the greatest influence on the phenotype of the Iqch KO mice." There is no evidence suggesting that the loss of SYNCRIP, HNRNPK, FUS, EWSR1, ANXA7, SLC25A4, and HNRPAB leads to Iqch KO phenotype.

Response: We apologize for our inaccurate statement. According to the literature, Fus KO, Ewsr1 KO, and Hnrnpk KO male mice were infertile, showing the spermatogenic arrest with absence of spermatozoa (Kuroda et al. 2000; Tian et al. 2021; Xu et al. 2022). Syncrip is involved meiotic process in Drosophila by interacting with Doublefault (Sechi et al. 2019). HNRPAB might be associated with mouse spermatogenesis by binding to Protamine 2 and contributing its translational regulation. Specifically, ANXA7 is a calcium-dependent phospholipid-binding protein that is a negative regulator of mitochondrial apoptosis (Du et al. 2015). Loss of SLC25A4 results in mitochondrial energy metabolism defects in mice (Graham et al. 1997). Moreover, RNA immunoprecipitation on formaldehyde cross-linked sperm followed by qPCR detected the interactions between HNRPAB and Catsper1, Catsper2, Catsper3, Ccdc40, Ccdc39, Ccdc65, Dnah8, Irrc6, and Dnhd1, which are essential for sperm development (Fukuda et al. 2013). Our Iqch KO mice showed abnormal sperm count, motility, morphology, and mitochondria, so we inferenced that IQCH might play a role in spermatogenesis by regulating the expression of SYNCRIP, HNRNPK, FUS, EWSR1, ANXA7, SLC25A4, and HNRPAB to some extent. We have changed an appropriate stamen that “We focused on SYNCRIP, HNRNPK, FUS, EWSR1, ANXA7, SLC25A4, and HNRPAB, which play important roles in spermatogenesis.”

(10) Fig. 6C and 6D use different styles of error bars.

Response: We are sorry for our oversight. In accordance with the reviewer's recommendations, we have modified the representation of error bars in the revised Fig. 6C.

(11) Line 296 to 297, "As expected, CaM interacted with IQCH, as indicated by LC-MS/MS analysis". It is not clear how LC-MS/MS detects protein interaction.

Response: As reviewer’s suggestions, we have supplemented the method details of LC-MS/MS experiment in the Methods section of revised manuscript. The results of proteins interacting with IQCH in sperm lysates from the LC-MS/MS experiment analysis were submitted as Figure 5—source data 1.

(12) It is still not clear how the interaction between IQCH, CaM, and HNRPAB is required for the expression of each other.

Response: Thank you for the reviewer’s comment. IQCH is a calmodulin-binding protein, and the binding of IQCH and CaM was confirmed by LC-MS/MS analysis and co-IP assay using sperm lysate. We thus speculated that if the interaction of IQCH and CaM might be a prerequisite for IQCH function. To prove that speculation, we took HNRPAB as an example. We knocked down IQCH in cultured cells, and a decrease in the expression of HNRPAB was observed. Similarly, when we knocked down CaM in cultured cells, and a decrease in the expression of HNRPAB was also detected. However, these results cannot exclude that IQCH or CaM could regulate HNRPAB expression alone. To investigate that if IQCH or CaM could regulate HNRPAB expression alone, we overexpressed IQCH in cells that knocked down CaM, while the expression of HNRPAB cannot be rescued, suggesting that IQCH cannot regulate HNRPAB expression when CaM is reduced. In consistent, we overexpressed CaM in cells that knocked down IQCH, while the expression of HNRPAB cannot be rescued, suggesting that CaM cannot regulate HNRPAB expression when IQCH is reduced. Thus, IQCH or CaM cannot regulate HNRPAB expression alone. Moreover, we deleted the IQ motif of IQCH, which is required for binding to CaM. The co-IP results showed that the interaction of IQCH and CaM was disrupted when deleting the IQ motif of IQCH, and the expression of HNRPAB was decreased. Therefore, we suggested that the interaction of IQCH and CaM might be required for IQCH regulating HNRPAB. In future studies, we will further investigate the relationships among IQCH, CaM, and HNRPAB.

Reviewer #3 (Recommendations For The Authors):

The authors have addressed my minor concerns. However, they neglected to address any of my more significant concerns in the public review. I assume that they simply overlooked these critiques, despite the fact that eLife explicitly states that "...as a general rule, concerns about a claim not being justified by the data should be explained in the public review." Therefore, the authors should have looked more carefully at the public reviews. As a result, my major concerns about the manuscript remain.

Response: We apologize for overlooking the public review process. We have improved our study based on the feedback received during the public review.

Author response:

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

eLife assessment

This important study advances our understanding of why diabetes is a risk factor for more severe Covid-19 disease. The authors offer solid evidence that cathepsin L is more active in diabetic individuals, that this higher activity is recapitulated at the cellular level in the presence of high glucose, and that high glucose leads to higher cathepsin L maturation. While not all aspects of the relationship between diabetes and cathepsin L (e.g., effects of metabolic acidosis) have been investigated, the work should be of interest to researchers in diabetes, virology, and immunology.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The study by He et al. investigates the relationship of an increased susceptibility of diabetes patients to COVID-19. The paper raises the possibility that hyperglycemia-induced cathepsin L maturation could be one of the driving forces in this pathology, suggesting that an increased activity of CTSL leads to accelerated virus infection rates due to an elevated processing of the SARS-CoV-2 spike protein.

In a clinical case-control study, the team found that the severity of corona infections was higher in diabetic patients, and their CTSL levels correlated well with the progression of the disease. They further showed an increase in CTSL activity in the long term as well as acute hyperglycemia. SARS-CoV-2 increasingly infected cells that were cultured in serum from diabetic patients, the same was observed using high glucose medium. No effect was observed in the medium with increased concentrations of insulin. CTSL knockout abolished the glucose-dependent increase in infection.

Increased glucose levels did not correlate with an increase in CTSL transcription. Rather He et al. could show that high glucose levels led to CTSL translocation from the ER into the lysosome. It was the glucose-dependent processing of the protease to its active form which promoted infection.

Strengths:

It is a complete study starting from a clinical observation and ending on the molecular mechanism. A strength is certainly the wide selection of experiments. The clinical study to investigate the effect of glucose on CTSL concentrations in healthy individuals sets the stage for experiments in cell culture, animal models, and human tissue. The effect of CTSL knockout cell lines on glucose-induced SARS-CoV2 infection rates is convincing. Finally, the team used a combination of Western blots and confocal microscopy to identify the underlying molecular mechanisms. The authors manage to keep the diabetic condition at the center of their study and therefore extend on previous knowledge of glucose-induced CTSL activation and their consequences for COVID-19 infections. By doing so, they create a novel connection between CTSL involvement in SARS-CoV2 infections and diabetes.

Weaknesses:

(1) The authors suggest that hyperglycemia as a symptom of diabetes leads to an increased infection rate in those patients. Throughout their study, the team focuses on two select symptoms of a diabetic condition, hyperglycemia and hyperinsulinemia. The team acknowledges in the discussion that there could be various other reasons. Hyperglycemia can lead to metabolic acidosis and a shift in blood pH. As CTSL activity is highly dependent on pH, it would have been crucial to include this parameter in the study.

We sincerely appreciate your valuable comment. We agree that hyperglycemia can lead to metabolic acidosis and alter blood pH. However, the normal range for blood pH in humans is relatively narrow, typically ranging from 7.35 to 7.45. In our study, we ensured that blood pH remained within this normal range for both diabetic and healthy control samples. To address your concern, we conducted experiments to investigate CTSL activity in response to pH fluctuations within this physiological range. The updated Fig. 4a now presents these findings, demonstrating consistent CTSL activity despite pH variations. Statistical analysis was performed using one-way ANOVA with Tukey’s post hoc test to ensure robustness. We have also amended the figure legend and provided corresponding descriptions in the final edition manuscript (line 15-18, page 7).

Author response image 1.

(2) The study rarely differentiates between cellular and extracellular CTSL activity. A more detailed explanation for the connection between the intracellular CTSL and serum CTSL in diabetic individuals, presumably via lysosomal exocytosis, could be helpful with regard to the final model to give a more complete picture.

Thank you for your insightful comments. Previous studies have elucidated the process by which lysosomal CTSL is transported via vesicles and subsequently secreted from the cell membrane through exocytosis (references 1-5). To provide a more comprehensive understanding, we have incorporated this information on Fig. 6h, page 32 of the final edition manuscript. This addition aims to enhance clarity regarding the connection between intracellular and serum CTSL activity in diabetic individuals, particularly through lysosomal exocytosis.

Author response image 2.

References：

(1) Reddy A et al. Plasma membrane repair is mediated by Ca(2+)-regulated exocytosis of lysosomes. Cell. 2001 Jul 27;106(2):157-69. doi: 10.1016/s0092-8674(01)00421-4. PMID: 11511344.

(2) Hasanagic M et al. Different Pathways to the Lysosome: Sorting out Alternatives. Int Rev Cell Mol Biol. 2015;320:75-101. doi: 10.1016/bs.ircmb.2015.07.008. Epub 2015 Aug 19. PMID: 26614872.

(3) Reiser J et al. Specialized roles for cysteine cathepsins in health and disease. J Clin Invest. 2010 Oct;120(10):3421-31. doi: 10.1172/JCI42918. Epub 2010 Oct 1. PMID: 20921628; PMCID: PMC2947230.

(4) Jaiswal JK et al. Membrane proximal lysosomes are the major vesicles responsible for calcium-dependent exocytosis in nonsecretory cells. J Cell Biol. 2002 Nov 25;159(4):625-35. doi: 10.1083/jcb.200208154. Epub 2002 Nov 18. PMID: 12438417; PMCID: PMC2173094.

(5) Coutinho MF et al. Mannose-6-phosphate pathway: a review on its role in lysosomal function and dysfunction. Mol Genet Metab. 2012 Apr;105(4):542-50. doi: 10.1016/j.ymgme.2011.12.012. Epub 2011 Dec 23. PMID: 22266136.

(3) In the early result section, an effect of hyperglycemia on total CTSL concentrations is described, but the data is not very convincing. Over the course of the manuscript, the hypothesis shifts increasingly towards an increase in protease trans-localization and processing to the active form rather than a change in total protease amounts. The overall importance of CTSL concentrations remains questionable.

Thank you for your insightful feedback. We have addressed your concerns regarding the impact of hyperglycemia on CTSL concentrations. Fig. 2h-j illustrate the effect of acute hyperglycemia on both CTSL concentration and activity in 15 healthy male volunteers over a 160-minute period. During this short timeframe, CTSL concentration remained stable, as evidenced by consistent RNA results from cells exposed to varying glucose levels (Supplementary Fig.1). However, there was a significant increase in CTSL activity, indicating that glucose elevation rapidly triggers CTSL maturation through propeptide cleavage. This activation process occurs more rapidly than CTSL protein synthesis. In summary, acute hyperglycemia specifically elevates CTSL activity, while chronic hyperglycemia may impact both CTSL activity and concentration (Fig. 2a-d). Additionally, Tournu C, et al. (1998) (reference 1) and Shi Q, et al. (2018) (reference 2) have reported that increased glucose metabolism promotes the maturation and secretion of CTSL and other proteases. These findings align with our evidence that hyperglycemia drives CTSL maturation, as discussed at line 10-25, page 12 in the final edition manuscript.

References：

(1) Tournu C et al. Glucose controls cathepsin expression in Ras-transformed fibroblasts. Arch Biochem Biophys. 1998 Dec 1;360(1):15-24. doi: 10.1006/abbi.1998.0916. PMID: 9826424.

(2) Shi Q et al. Increased glucose metabolism in TAMs fuels O-GlcNAcylation of lysosomal Cathepsin B to promote cancer metastasis and chemoresistance. Cancer Cell. 2022 Oct 10;40(10):1207-1222.e10. doi: 10.1016/j.ccell.2022.08.012. Epub 2022 Sep 8. PMID: 36084651.

Reviewer #2 (Public Review):

Summary:

In this study, the authors hypothesized that individuals with diabetes have elevated blood CTSL levels, which facilitates SARS-CoV-2 infection. The authors conducted in vitro experiments, revealing that elevated glucose levels promote SARS-CoV-2 infection in wild-type cells. In contrast, CTSL knockout cells show reduced susceptibility to high glucose-promoted effects. Additionally, the authors utilized lung tissue samples obtained from both diabetic and non-diabetic patients, along with db/db diabetic and control mice. Their findings indicate that diabetic conditions lead to an elevation in CTSL activity in both humans and mice.

Strengths:

The authors have effectively met their research objectives, and their conclusions are supported by the data presented. Their findings suggest that high glucose levels promote CTSL maturation and translocation from the endoplasmic reticulum to the lysosome, potentially contributing to diabetic comorbidities and complications.

Weaknesses:

(1) In Figure 1e, the authors measured plasma levels of COVID-19 related proteins, including ACE2, CTSL, and CTSB, in both diabetic and non-diabetic COVID-19 patients. Notably, only CTSL levels exhibited a significant increase in diabetic patients compared to non-diabetic patients, and these levels varied throughout the course of COVID-19. Given that the diabetes groups encompass both male and female patients, it is essential to ascertain whether the authors considered the potential impact of gender on CTSL levels. The diabetes groups comprised a higher percentage of male patients (61.3%) compared to the non-diabetes group, where males constituted only 38.7%.

Thank you for your insightful feedback. In response to your concerns regarding the potential impact of gender on CTSL levels in diabetic and non-diabetic COVID-19 patients, we conducted analyses to address this issue. While our initial study involved 62 COVID-19 patients, with 31 having diabetes and 31 without, matching based on gender and age, we acknowledged the challenge of obtaining balanced gender distribution in both groups due to the difficulty of collecting blood samples from COVID-19 patients. To mitigate potential gender bias resulting from small sample sizes, we conducted a supplementary clinical study involving 122 non-COVID-19 volunteers, including 61 individuals with diabetes and 61 without. The percentage of males in the diabetes group was 50.8%, while in the healthy group, males constituted 44.3% (P value = 0.468), indicating no significant gender bias. We have incorporated this information into the discussion section on line 4-13, page 11 in the final edition manuscript, to provide clarity on this aspect of our study.

(2) Lines 145-149: "The results showed that WT Huh7 cell cultured in high glucose medium exhibited a much higher infective rate than those in low glucose medium. However, CTSL KO Huh7 cells maintained a low infective rate of SARS-CoV-2 regardless of glucose or insulin levels (Fig. 3f-h). Therefore, hyperglycemia enhanced SARS-CoV-2 infection dependent on CTSL." However, this evidence may be insufficient to support the claim that hyperglycemia enhances SARS-CoV-2 infection dependent on CTSL. The human hepatoma cell line Huh7 might not be an ideal model to validate the authors' hypothesis regarding high blood glucose promoting SARS-CoV-2 infection through CTSL.

Thank you for your valuable feedback. We have addressed the concerns regarding the sufficiency of evidence supporting the claim that hyperglycemia enhances SARS-CoV-2 infection dependent on CTSL. Specifically, we have revised the expression to state, “Therefore, hyperglycemia enhanced SARS-CoV-2 infection through CTSL.” as suggested, in line 9, page 7 in the final edition manuscript. Additionally, we acknowledge the potential involvement of other bioactive factors, such as 1,5-anhydro-D-glucitol (1,5-AG), in mediating SARS-CoV-2 infection in patients with diabetes, as outlined in the discussion section from line 13-21, page 13 in the final edition manuscript.

Regarding the choice of the human hepatoma cell line Huh7 as a model for investigating hyperglycemia-induced CTSL maturation and SARS-CoV-2 infection, we recognize the importance of tissue specificity and the liver’s significance as a target organ for COVID-19. Despite potential limitations, such as generalization of liver function abnormalities and lack of tissue specificity in SARS-CoV-2 impact, Huh7 cells offer practical advantages as a mature cell model for studying SARS-CoV-2 infection, including accessibility, susceptibility to infection, and stable proliferation (reference 1-3). We have elaborated on these considerations in the discussion section at line 19-23, page 11 in the final edition manuscript, to provide context for our choice of experimental model.

References：

(1) Gupta A et al. Extrapulmonary manifestations of COVID-19. Nat Med. 2020 Jul;26(7):1017-1032. doi: 10.1038/s41591-020-0968-3. Epub 2020 Jul 10. PMID: 32651579.

(2) Nie X et al. Multi-organ proteomic landscape of COVID-19 autopsies. Cell. 2021 Feb 4;184(3):775-791.e14. doi: 10.1016/j.cell.2021.01.004. Epub 2021 Jan 9. PMID: 33503446; PMCID: PMC7794601.

(3) Ciotti M et al. The COVID-19 pandemic. Crit Rev Clin Lab Sci. 2020 Sep;57(6):365-388. doi: 10.1080/10408363.2020.1783198. Epub 2020 Jul 9. PMID: 32645276.

(3) The Abstract and Introduction sections lack effective organization.

Thank you for your valuable comments. We have rewritten the Abstract and Introduction sections and incorporated the updated descriptions in the final edition manuscript.

Reviewer #1 (Recommendations For The Authors):

(1) When referring to diabetes, does this exclusively include diabetes type 2?

Thank you for your inquiry. In our study, the term “diabetes” encompasses the condition of hyperglycemia in a broad sense, rather than specifically indicating type 1 diabetes (T1DM) or type 2 diabetes (T2DM). This broader definition aligns with the scope of our research objectives and findings, particularly observed in the cell experiments conducted. We have clarified this point in the revised discussion section, from line 6-9, page 12 in the final edition manuscript, to provide additional context for readers.

(2) The titles of the individual paragraphs are not very strong and descriptive. More precise titles help to structure the paper better for the reader.

Thank you for your valuable comments. We have rewritten the title of each section to make it more precise for readers and incorporated the updated descriptions in the manuscript.

(3) Fig.3c, adding a 0 nM insulin control would be nice.

Thank you for your suggestion. We have revised Fig.3c according to your advice. The revised figure was located at page 29 in the final edition manuscript. The corresponding figure legend has also been revised.

Author response image 3.

(4) Fig.3e non-infection control would be nice.

Thank you for your suggestion. We have incorporated your feedback by adding a non-infection control in Fig. 3e. In this revised figure, we included a measurement of SARS-CoV-2 pseudovirus infection assessed through the fluorescence captured by a reader. Cells infected by the pseudovirus exhibited activation of the firefly luciferase, resulting in the release of fluorescence. Conversely, non-infected control cells showed no fluorescence, with the reader recording a value of zero. The updated figure can now be found on page 29 in the final edition manuscript, and we have adjusted the corresponding figure legend accordingly.

Author response image 4.

(5) In Figure 5, the processing of CTSL in cells (b-c) strongly differs from processing in tissue (d-e) focusing on amounts of dc-mCTSL. Do you have an explanation for this? Overall, blots are hard to judge by eye and it would be nice to include blots with shorter exposure.

Thank you for your insightful feedback. The differences observed in the processing of CTSL between cells (Fig. 5b) and tissues (Fig. 5d-e) may be attributed to the complexities inherent in tissue samples, which can impact the clarity of the images. Furthermore, in human tissue samples, it is pertinent to consider that patients in the diabetes group had their blood glucose levels controlled within or near the normal range prior to lung surgery. As a result, the evidence supporting CTSL maturation in human lung tissue blotting images may be less compelling. We have addressed this aspect in the revised results section (lines 10-13, page 9). Additionally, we will consider including blots with shorter exposure to enhance visual clarity in future studies.

(6) Considering Fig2B and Figure S1, the evidence of an effect of hyperglycemia or high glucose medium on total CTSL protein concentration is not very strong. In my opinion, this claim in the results section for Fig2 should be revisited.

Thank you for your valuable suggestion. We have revisited the section in question and made appropriate revisions. The original sentence has been modified to accurately reflect the findings: "We found that plasma CTSL activity was strongly positively correlated with chronic hyperglycemia indicated by HbA1c and was significantly higher in diabetic patients than in euglycemic individuals (Fig. 2a, c). Additionally, plasma CTSL concentration showed a positive trend with chronic hyperglycemia indicated by HbA1c (Fig. 2b, d)". These changes have been incorporated into the revised results section (lines 12-16, page 5).

(7) Overall, data hinting to increased CTSL activity is stronger than protein amount. This being said, in hyperglycemia, blood pH can be affected (metabolic acidosis). As CTSL has higher activity at low pH, could the increase in activity be caused by a drop in pH? Can you include this aspect in your manuscript? For example, is there a pH difference in serum of nondiabetic vs diabetic patients?

Thank you for your valuable input. We have already addressed the potential impact of pH changes on CTSL activity in our response to Weakness No. 1. As indicated, although hyperglycemia can lead to metabolic acidosis and changes in blood pH, the pH levels observed in our study remained within the normal range (7.35 to 7.45). Therefore, we conducted experiments to investigate CTSL activity in response to changes in pH, which showed consistent activity levels within this range. This information has been included in our revised manuscript (line 15-18, page 7).

Reviewer #2 (Recommendations For The Authors):

(1) The Abstract and Introduction sections lack effective organization. The manuscript's style resembles that of Cell Journal rather than aligning with the customary format of eLife.

Thank you for your valuable comments. The Abstract and Introduction sections have been reorganized to be more precise for readers has been included in our revised manuscript. Additionally, we have meticulously updated the manuscript's style to align with the standard format of eLife in our revised manuscript, especially key resources table of materials and methods sections.

Author response:

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

Reviewer #1 (Public Review):

Strengths:

The study was designed as a 6-month follow-up, with repeated behavioral and EEG measurements through disease development, providing valuable and interesting findings on AD progression and the effect of early-life choline supplantation. Moreover, the behavioral data that suggest an adverse effect of low choline in WT mice are interesting and important beyond the context of AD.

Thank you for identifying several strengths.

Weaknesses:

(1) The multiple headings and subheadings, focusing on the experimental method rather than the narrative, reduce the readability.

We have reduced the number of headings.

(2) Quantification of NeuN and FosB in WT littermates is needed to demonstrate rescue of neuronal death and hyperexcitability by high choline supplementation and also to gain further insights into the adverse effect of low choline on the performance of WT mice in the behavioral test.

We agree and have added WT data for the NeuN and ΔFosB analyses. These data are included in the text and figures. For NeuN, the Figure is Figure 6. For ΔFosB it is Figure 7. In brief, the high choline diet restored NeuN and ΔFosB to the levels of WT mice.

Below is Figure 6 and its legend to show the revised presentation of data for NeuN. Afterwards is the revised figure showing data for ΔFosB. After that are the sections of the Results that have been revised.

Author response image 1.

Choline supplementation improved NeuN immunoreactivity (ir) in hilar cells in Tg2576 animals. A. Representative images of NeuN-ir staining in the anterior DG of Tg2576 animals. (1) A section from a Tg2576 mouse fed the low choline diet. The area surrounded by a box is expanded below. Red arrows point to NeuN-ir hilar cells. Mol=molecular layer, GCL=granule cell layer, HIL=hilus. Calibration for the top row, 100 µm; for the bottom row, 50 µm. (2) A section from a Tg2576 mouse fed the intermediate diet. Same calibrations as for 1. (3) A section from a Tg2576 mouse fed the high choline diet. Same calibrations as for 1. B. Quantification methods. Representative images demonstrate the thresholding criteria used to quantify NeuN-ir. (1) A NeuN-stained section. The area surrounded by the white box is expanded in the inset (arrow) to show 3 hilar cells. The 2 NeuN-ir cells above threshold are marked by blue arrows. The 1 NeuN-ir cell below threshold is marked by a green arrow. (2) After converting the image to grayscale, the cells above threshold were designated as red. The inset shows that the two cells that were marked by blue arrows are red while the cell below threshold is not. (3) An example of the threshold menu from ImageJ showing the way the threshold was set. Sliders (red circles) were used to move the threshold to the left or right of the histogram of intensity values. The final position of the slider (red arrow) was positioned at the onset of the steep rise of the histogram. C. NeuN-ir in Tg2576 and WT mice. Tg2576 mice had either the low, intermediate, or high choline diet in early life. WT mice were fed the standard diet (intermediate choline). (1) Tg2576 mice treated with the high choline diet had significantly more hilar NeuN-ir cells in the anterior DG compared to Tg2576 mice that had been fed the low choline or intermediate diet. The values for Tg2576 mice that received the high choline diet were not significantly different from WT mice, suggesting that the high choline diet restored NeuN-ir. (2) There was no effect of diet or genotype in the posterior DG, probably because the low choline and intermediate diet did not appear to lower hilar NeuN-ir.

Author response image 2.

Choline supplementation reduced ∆FosB expression in dorsal GCs of Tg2576 mice. A. Representative images of ∆FosB staining in GCL of Tg2576 animals from each treatment group. (1) A section from a low choline-treated mouse shows robust ∆FosB-ir in the GCL. Calibration, 100 µm. Sections from intermediate (2) and high choline (3)-treated mice. Same calibration as 1. B. Quantification methods. Representative images demonstrating the thresholding criteria established to quantify ∆FosB. (1) A ∆FosB -stained section shows strongly-stained cells (white arrows). (2) A strict thresholding criteria was used to make only the darkest stained cells red. C. Use of the strict threshold to quantify ∆FosB-ir. (1) Anterior DG. Tg2576 mice treated with the choline supplemented diet had significantly less ∆FosB-ir compared to the Tg2576 mice fed the low or intermediate diets. Tg2576 mice fed the high choline diet were not significantly different from WT mice, suggesting a rescue of ∆FosB-ir. (2) There were no significant differences in ∆FosB-ir in posterior sections. D. Methods are shown using a threshold that was less strict. (1) Some of the stained cells that were included are not as dark as those used for the strict threshold (white arrows). (2) All cells above the less conservative threshold are shown in red. E. Use of the less strict threshold to quantify ∆FosB-ir. (1) Anterior DG. Tg2576 mice that were fed the high choline diet had less ΔFosB-ir pixels than the mice that were fed the other diets. There were no differences from WT mice, suggesting restoration of ∆FosB-ir by choline enrichment in early life. (2) Posterior DG. There were no significant differences between Tg2576 mice fed the 3 diets or WT mice.

Results, Section C1, starting on Line 691:

“To ask if the improvement in NeuN after MCS in Tg256 restored NeuN to WT levels we used WT mice. For this analysis we used a one-way ANOVA with 4 groups: Low choline Tg2576, Intermediate Tg2576, High choline Tg2576, and Intermediate WT (Figure 5C). Tukey-Kramer multiple comparisons tests were used as the post hoc tests. The WT mice were fed the intermediate diet because it is the standard mouse chow, and this group was intended to reflect normal mice. The results showed a significant group difference for anterior DG (F(3,25)=9.20; p=0.0003; Figure 5C1) but not posterior DG (F(3,28)=0.867; p=0.450; Figure 5C2). Regarding the anterior DG, there were more NeuN-ir cells in high choline-treated mice than both low choline (p=0.046) and intermediate choline-treated Tg2576 mice (p=0.003). WT mice had more NeuN-ir cells than Tg2576 mice fed the low (p=0.011) or intermediate diet (p=0.003). Tg2576 mice that were fed the high choline diet were not significantly different from WT (p=0.827).”

Results, Section C2, starting on Line 722:

“There was strong expression of ∆FosB in Tg2576 GCs in mice fed the low choline diet (Figure 7A1). The high choline diet and intermediate diet appeared to show less GCL ΔFosB-ir (Figure 7A2-3). A two-way ANOVA was conducted with the experimental group (Tg2576 low choline diet, Tg2576 intermediate choline diet, Tg2576 high choline diet, WT intermediate choline diet) and location (anterior or posterior) as main factors. There was a significant effect of group (F(3,32)=13.80, p=<0.0001) and location (F(1,32)=8.69, p=0.006). Tukey-Kramer post-hoc tests showed that Tg2576 mice fed the low choline diet had significantly greater ΔFosB-ir than Tg2576 mice fed the high choline diet (p=0.0005) and WT mice (p=0.0007). Tg2576 mice fed the low and intermediate diets were not significantly different (p=0.275). Tg2576 mice fed the high choline diet were not significantly different from WT (p>0.999). There were no differences between groups for the posterior DG (all p>0.05).”

“∆FosB quantification was repeated with a lower threshold to define ∆FosB-ir GCs (see Methods) and results were the same (Figure 7D). Two-way ANOVA showed a significant effect of group (F(3,32)=14.28, p< 0.0001) and location (F(1,32)=7.07, p=0.0122) for anterior DG but not posterior DG (Figure 7D). For anterior sections, Tukey-Kramer post hoc tests showed that low choline mice had greater ΔFosB-ir than high choline mice (p=0.0024) and WT mice (p=0.005) but not Tg2576 mice fed the intermediate diet (p=0.275); Figure 7D1). Mice fed the high choline diet were not significantly different from WT (p=0.993; Figure 7D1). These data suggest that high choline in the diet early in life can reduce neuronal activity of GCs in offspring later in life. In addition, low choline has an opposite effect, suggesting low choline in early life has adverse effects.”

(3) Quantification of the discrimination ratio of the novel object and novel location tests can facilitate the comparison between the different genotypes and diets.

We have added the discrimination index for novel object location to the paper. The data are in a new figure: Figure 3. In brief, the results for discrimination index are the same as the results done originally, based on the analysis of percent of time exploring the novel object.

Below is the new Figure and legend, followed by the new text in the Results.

Author response image 3.

Novel object location results based on the discrimination index. A. Results are shown for the 3 months-old WT and Tg2576 mice based on the discrimination index. (1) Mice fed the low choline diet showed object location memory only in WT. (2) Mice fed the intermediate diet showed object location memory only in WT. (3) Mice fed the high choline diet showed memory both for WT and Tg2576 mice. Therefore, the high choline diet improved memory in Tg2576 mice. B. The results for the 6 months-old mice are shown. (1-2) There was no significant memory demonstrated by mice that were fed either the low or intermediate choline diet. (3) Mice fed a diet enriched in choline showed memory whether they were WT or Tg2576 mice. Therefore, choline enrichment improved memory in all mice.

Results, Section B1, starting on line 536:

“The discrimination indices are shown in Figure 3 and results led to the same conclusions as the analyses in Figure 2. For the 3 months-old mice (Figure 3A), the low choline group did not show the ability to perform the task for WT or Tg2576 mice. Thus, a two-way ANOVA showed no effect of genotype (F(1,74)=0.027, p=0.870) or task phase (F(1,74)=1.41, p=0.239). For the intermediate diet-treated mice, there was no effect of genotype (F(1,50)=0.3.52, p=0.067) but there was an effect of task phase (F(1,50)=8.33, p=0.006). WT mice showed a greater discrimination index during testing relative to training (p=0.019) but Tg2576 mice did not (p=0.664). Therefore, Tg2576 mice fed the intermediate diet were impaired. In contrast, high choline-treated mice performed well. There was a main effect of task phase (F(1,68)=39.61, p=<0.001) with WT (p<0.0001) and Tg2576 mice (p=0.0002) showing preference for the moved object in the test phase. Interestingly, there was a main effect of genotype (F(1,68)=4.50, p=0.038) because the discrimination index for WT training was significantly different from Tg2576 testing (p<0.0001) and Tg2576 training was significantly different from WT testing (p=0.0003).”

“The discrimination indices of 6 months-old mice led to the same conclusions as the results in Figure 2. There was no evidence of discrimination in low choline-treated mice by two-way ANOVA (no effect of genotype, (F(1,42)=3.25, p=0.079; no effect of task phase, F(1,42)=0.278, p=0.601). The same was true of mice fed the intermediate diet (genotype, F(1,12)=1.44, p=0.253; task phase, F(1,12)=2.64, p=0.130). However, both WT and Tg2576 mice performed well after being fed the high choline diet (effect of task phase, (F(1,52)=58.75, p=0.0001, but not genotype (F(1,52)=1.197, p=0.279). Tukey-Kramer post-hoc tests showed that both WT (p<0.0001) and Tg2576 mice that had received the high choline diet (p=0.0005) had elevated discrimination indices for the test session.”

(4) The longitudinal analyses enable the performance of multi-level correlations between the discrimination ratio in NOR and NOL, NeuN and Fos levels, multiple EEG parameters, and premature death. Such analysis can potentially identify biomarkers associated with AD progression. These can be interesting in different choline supplementation, but also in the standard choline diet.

We agree and added correlations to the paper in a new figure (Figure 9). Below is Figure 9 and its legend. Afterwards is the new Results section.

Author response image 4.

Correlations between IIS, Behavior, and hilar NeuN-ir. A. IIS frequency over 24 hrs is plotted against the preference for the novel object in the test phase of NOL. A greater preference is reflected by a greater percentage of time exploring the novel object. (1) The mice fed the high choline diet (red) showed greater preference for the novel object when IIS were low. These data suggest IIS impaired object location memory in the high choline-treated mice. The low choline-treated mice had very weak preference and very few IIS, potentially explaining the lack of correlation in these mice. (2) There were no significant correlations for IIS and NOR. However, there were only 4 mice for the high choline group, which is a limitation. B. IIS frequency over 24 hrs is plotted against the number of dorsal hilar cells expressing NeuN. The dorsal hilus was used because there was no effect of diet on the posterior hilus. (1) Hilar NeuN-ir is plotted against the preference for the novel object in the test phase of NOL. There were no significant correlations. (2) Hilar NeuN-ir was greater for mice that had better performance in NOR, both for the low choline (blue) and high choline (red) groups. These data support the idea that hilar cells contribute to object recognition (Kesner et al. 2015; Botterill et al. 2021; GoodSmith et al. 2022).

Results, Section F, starting on Line 801:

“F. Correlations between IIS and other measurements

As shown in Figure 9A, IIS were correlated to behavioral performance in some conditions. For these correlations, only mice that were fed the low and high choline diets were included because mice that were fed the intermediate diet did not have sufficient EEG recordings in the same mouse where behavior was studied. IIS frequency over 24 hrs was plotted against the preference for the novel object in the test phase (Figure 9A). For NOL, IIS were significantly less frequent when behavior was the best, but only for the high choline-treated mice (Pearson’s r, p=0.022). In the low choline group, behavioral performance was poor regardless of IIS frequency (Pearson’s r, p=0.933; Figure 9A1). For NOR, there were no significant correlations (low choliNe, p=0.202; high choline, p=0.680) but few mice were tested in the high choline-treated mice (Figure 9B2).

We also tested whether there were correlations between dorsal hilar NeuN-ir cell numbers and IIS frequency. In Figure 9B, IIS frequency over 24 hrs was plotted against the number of dorsal hilar cells expressing NeuN. The dorsal hilus was used because there was no effect of diet on the posterior hilus. For NOL, there was no significant correlation (low choline, p=0.273; high choline, p=0.159; Figure 9B1). However, for NOR, there were more NeuN-ir hilar cells when the behavioral performance was strongest (low choline, p=0.024; high choline, p=0.016; Figure 9B2). These data support prior studies showing that hilar cells, especially mossy cells (the majority of hilar neurons), contribute to object recognition (Botterill et al. 2021; GoodSmith et al. 2022).”

We also noted that all mice were not possible to include because they died or other reasons, such a a loss of the headset (Results, Section A, Lines 463-464): Some mice were not possible to include in all assays either because they died before reaching 6 months or for other reasons.

Reviewer #2 (Public Review):

Strengths:

The strength of the group was the ability to monitor the incidence of interictal spikes (IIS) over the course of 1.2-6 months in the Tg2576 Alzheimer's disease model, combined with meaningful behavioral and histological measures. The authors were able to demonstrate MCS had protective effects in Tg2576 mice, which was particularly convincing in the hippocampal novel object location task.

We thank the Reviewer for identifying several strengths.

Weaknesses:

Although choline deficiency was associated with impaired learning and elevated FosB expression, consistent with increased hyperexcitability, IIS was reduced with both low and high choline diets. Although not necessarily a weakness, it complicates the interpretation and requires further evaluation.

We agree and we revised the paper to address the evaluations that were suggested.

Reviewer #1 (Recommendations For The Authors):

(1) A reference directing to genotyping of Tg2576 mice is missing.

We apologize for the oversight and added that the mice were genotyped by the New York University Mouse Genotyping core facility.

Methods, Section A, Lines 210-211: “Genotypes were determined by the New York University Mouse Genotyping Core facility using a protocol to detect APP695.”

(2) Which software was used to track the mice in the behavioral tests?

We manually reviewed videos. This has been clarified in the revised manuscript. Methods, Section B4, Lines 268-270: Videos of the training and testing sessions were analyzed manually. A subset of data was analyzed by two independent blinded investigators and they were in agreement.

(3) Unexpectedly, a low choline diet in AD mice was associated with reduced frequency of interictal spikes yet increased mortality and spontaneous seizures. The authors attribute this to postictal suppression.

We did not intend to suggest that postictal depression was the only cause. It was a suggestion for one of many potential explanations why seizures would influence IIS frequency. For postictal depression, we suggested that postictal depression could transiently reduce IIS. We have clarified the text so this is clear (Discussion, starting on Line 960):

If mice were unhealthy, IIS might have been reduced due to impaired excitatory synaptic function. Another reason for reduced IIS is that the mice that had the low choline diet had seizures which interrupted REM sleep. Thus, seizures in Tg2576 mice typically started in sleep. Less REM sleep would reduce IIS because IIS occur primarily in REM. Also, seizures in the Tg2576 mice were followed by a depression of the EEG (postictal depression; Supplemental Figure 3) that would transiently reduce IIS. A different, radical explanation is that the intermediate diet promoted IIS rather than low choline reducing IIS. Instead of choline, a constituent of the intermediate diet may have promoted IIS.

However, reduced spike frequency is already evident at 5 weeks of age, a time point with a low occurrence of premature death. A more comprehensive analysis of EEG background activity may provide additional information if the epileptic activity is indeed reduced at this age.

We did not intend to suggest that premature death caused reduced spike frequency. We have clarified the paper accordingly. We agree that a more in-depth EEG analysis would be useful but is beyond the scope of the study.

(4) Supplementary Fig. 3 depicts far more spikes / 24 h compared to Fig. 7B (at least 100 spikes/24h in Supplementary Fig. 3 and less than 10 spikes/24h in Fig. 7B).

We would like to clarify that before and after a seizure the spike frequency is unusually high. Therefore, there are far more spikes than prior figures.

We clarified this issue by adding to the Supplemental Figure more data. The additional data are from mice without a seizure, showing their spikes are low in frequency.

All recordings lasted several days. We included the data from mice with a seizure on one of the days and mice without any seizures. For mice with a seizure, we graphed IIS frequency for the day before, the day of the seizure, and the day after. For mice without a seizure, IIS frequency is plotted for 3 consecutive days. When there was a seizure, the day before and after showed high numbers of spikes. When there was no seizure on any of the 3 days, spikes were infrequent on all days.

The revised figure and legend are shown below. It is Supplemental Figure 4 in the revised submission.

Author response image 5.

IIS frequency before and after seizures. A. Representative EEG traces recorded from electrodes implanted in the skull over the left frontal cortex, right occipital cortex, left hippocampus (Hippo) and right hippocampus during a spontaneous seizure in a 5 months-old Tg2576 mouse. Arrows point to the start (green arrow) and end of the seizure (red arrow), and postictal depression (blue arrow). B. IIS frequency was quantified from continuous video-EEG for mice that had a spontaneous seizure during the recording period and mice that did not. IIS frequency is plotted for 3 consecutive days, starting with the day before the seizure (designated as day 1), and ending with the day after the seizure (day 3). A two-way RMANOVA was conducted with the day and group (mice with or without a seizure) as main factors. There was a significant effect of day (F(2,4)=46.95, p=0.002) and group (seizure vs no seizure; F(1,2)=46.01, p=0.021) and an interaction of factors (F(2,4)=46.68, p=0.002)..Tukey-Kramer post-hoc tests showed that mice with a seizure had significantly greater IIS frequencies than mice without a seizure for every day (day 1, p=0.0005; day 2, p=0.0001; day 3, p=0.0014). For mice with a seizure, IIS frequency was higher on the day of the seizure than the day before (p=0.037) or after (p=0.010). For mice without a seizure, there were no significant differences in IIS frequency for day 1, 2, or 3. These data are similar to prior work showing that from one day to the next mice without seizures have similar IIS frequencies (Kam et al., 2016).

In the text, the revised section is in the Results, Section C, starting on Line 772:

“At 5-6 months, IIS frequencies were not significantly different in the mice fed the different diets (all p>0.05), probably because IIS frequency becomes increasingly variable with age (Kam et al. 2016). One source of variability is seizures, because there was a sharp increase in IIS during the day before and after a seizure (Supplemental Figure 4). Another reason that the diets failed to show differences was that the IIS frequency generally declined at 5-6 months. This can be appreciated in Figure 8B and Supplemental Figure 6B. These data are consistent with prior studies of Tg2576 mice where IIS increased from 1 to 3 months but then waxed and waned afterwards (Kam et al., 2016).”

(5) The data indicating the protective effect of high choline supplementation are valuable, yet some of the claims are not completely supported by the data, mainly as the analysis of littermate WT mice is not complete.

We added WT data to show that the high choline diet restored cell loss and ΔFosB expression to WT levels. These data strengthen the argument that the high choline diet was valuable. See the response to Reviewer #1, Public Review Point #2.

• Line 591: "The results suggest that choline enrichment protected hilar neurons from NeuN loss in Tg2576 mice." A comparison to NeuN expression in WT mice is needed to make this statement.

These data have been added. See the response to Reviewer #1, Public Review Point #2.

• Line 623: "These data suggest that high choline in the diet early in life can reduce hyperexcitability of GCs in offspring later in life. In addition, low choline has an opposite effect, again suggesting this maternal diet has adverse effects." Also here, FosB quantification in WT mice is needed.

These data have been added. See the response to Reviewer #1, Public Review Point #2.

(7) Was the effect of choline associated with reduced tauopathy or A levels?

The mice have no detectable hyperphosphorylated tau. The mice do have intracellular A before 6 months. This is especially the case in hilar neurons, but GCs have little (Criscuolo et al., eNeuro, 2023). However, in neurons that have reduced NeuN, we found previously that antibodies generally do not work well. We think it is because the neurons become pyknotic (Duffy et al., 2015), a condition associated with oxidative stress which causes antigens like NeuN to change conformation due to phosphorylation. Therefore, we did not conduct a comparison of hilar neurons across the different diets.

(8) Since the mice were tested at 3 months and 6 months, it would be interesting to see the behavioral difference per mouse and the correlation with EEG recording and immunohistological analyses.

We agree that would be valuable and this has been added to the paper. Please see response to Reviewer #1, Public Review Point #4.

Reviewer #2 (Recommendations For The Authors):

There were several areas that could be further improved, particularly in the areas of data analysis (particularly with images and supplemental figures), figure presentation, and mechanistic speculation.

Major points:

(1) It is understandable that, for the sake of labor and expense, WT mice were not implanted with EEG electrodes, particularly since previous work showed that WT mice have no IIS (Kam et al. 2016). However, from a standpoint of full factorial experimental design, there are several flaws - purists would argue are fatal flaws. First, the lack of WT groups creates underpowered and imbalanced groups, constraining statistical comparisons and likely reducing the significance of the results. Also, it is an assumption that diet does not influence IIS in WT mice. Secondly, with a within-subject experimental design (as described in Fig. 1A), 6-month-old mice are not naïve if they have previously been tested at 3 months. Such an experimental design may reduce effect size compared to non-naïve mice. These caveats should be included in the Discussion. It is likely that these caveats reduce effect size and that the actual statistical significance, were the experimental design perfect, would be higher overall.

We agree and have added these points to the Limitations section of the Discussion. Starting on Line 1050: In addition, groups were not exactly matched. Although WT mice do not have IIS, a WT group for each of the Tg2576 groups would have been useful. Instead, we included WT mice for the behavioral tasks and some of the anatomical assays. Related to this point is that several mice died during the long-term EEG monitoring of IIS.

(2) Since behavior, EEG, NeuN and FosB experiments seem to be done on every Tg2576 animal, it seems that there are missed opportunities to correlate behavior/EEG and histology on a per-mouse basis. For example, rather than speculate in the discussion, why not (for example) directly examine relationships between IIS/24 hours and FosB expression?

We addressed this point above in responding to Reviewer #1, Public Review Point #4.

(3) Methods of image quantification should be improved. Background subtraction should be considered in the analysis workflow (see Fig. 5C and Fig. 6C background). It would be helpful to have a Methods figure illustrating intermediate processing steps for both NeuN and FosB expression.

We added more information to improve the methods of quantification. We did use a background subtraction approach where ImageJ provides a histogram of intensity values, and it determines when there is a sharp rise in staining relative to background. That point is where we set threshold. We think it is a procedure that has the least subjectivity.

We added these methods to the Methods section and expanded the first figure about image quantification, Figure 6B. That figure and legend are shown above in response to Reviewer #1, Point #2.

This is the revised section of the Methods, Section C3, starting on Line 345:

“Photomicrographs were acquired using ImagePro Plus V7.0 (Media Cybernetics) and a digital camera (Model RET 2000R-F-CLR-12, Q-Imaging). NeuN and ∆FosB staining were quantified from micrographs using ImageJ (V1.44, National Institutes of Health). All images were first converted to grayscale and in each section, the hilus was traced, defined by zone 4 of Amaral (1978). A threshold was then calculated to identify the NeuN-stained cell bodies but not background. Then NeuN-stained cell bodies in the hilus were quantified manually. Note that the threshold was defined in ImageJ using the distribution of intensities in the micrograph. A threshold was then set using a slider in the histogram provided by Image J. The slider was pushed from the low level of staining (similar to background) to the location where staining intensity made a sharp rise, reflecting stained cells. Cells with labeling that was above threshold were counted.”

(4) This reviewer is surprised that the authors do not speculate more about ACh-related mechanisms. For example, choline deficiency would likely reduce Ach release, which could have the same effect on IIS as muscarinic antagonism (Kam et al. 2016), and could potentially explain the paradoxical effects of a low choline diet on reducing IIS. Some additional mechanistic speculation would be helpful in the Discussion.

We thank the Reviewer for noting this so we could add it to the Discussion. We had not because we were concerned about space limitations.

The Discussion has a new section starting on Line 1009:

“Choline and cholinergic neurons

There are many suggestions for the mechanisms that allow MCS to improve health of the offspring. One hypothesis that we are interested in is that MCS improves outcomes by reducing IIS. Reducing IIS would potentially reduce hyperactivity, which is significant because hyperactivity can increase release of A. IIS would also be likely to disrupt sleep since it represents aberrant synchronous activity over widespread brain regions. The disruption to sleep could impair memory consolidation, since it is a notable function of sleep (Graves et al. 2001; Poe et al. 2010). Sleep disruption also has other negative consequences such as impairing normal clearance of A (Nedergaard and Goldman 2020). In patients, IIS and similar events, IEDs, are correlated with memory impairment (Vossel et al. 2016).

How would choline supplementation in early life reduce IIS of the offspring? It may do so by making BFCNs more resilient. That is significant because BFCN abnormalities appear to cause IIS. Thus, the cholinergic antagonist atropine reduced IIS in vivo in Tg2576 mice. Selective silencing of BFCNs reduced IIS also. Atropine also reduced elevated synaptic activity of GCs in young Tg2576 mice in vitro. These studies are consistent with the idea that early in AD there is elevated cholinergic activity (DeKosky et al. 2002; Ikonomovic et al. 2003; Kelley et al. 2014; Mufson et al. 2015; Kelley et al. 2016), while later in life there is degeneration. Indeed, the chronic overactivity could cause the degeneration.

Why would MCS make BFCNs resilient? There are several possibilities that have been explored, based on genes upregulated by MCS. One attractive hypothesis is that neurotrophic support for BFCNs is retained after MCS but in aging and AD it declines (Gautier et al. 2023). The neurotrophins, notably nerve growth factor (NGF) and brain-derived neurotrophic factor (BDNF) support the health of BFCNs (Mufson et al. 2003; Niewiadomska et al. 2011).”

Minor points:

(1) The vendor is Dyets Inc., not Dyets.

Thank you. This correction has been made.

(2) Anesthesia chamber not specified (make, model, company).

We have added this information to the Methods, Section D1, starting on Line 375: The animals were anesthetized by isoflurane inhalation (3% isoflurane. 2% oxygen for induction) in a rectangular transparent plexiglas chamber (18 cm long x 10 cm wide x 8 cm high) made in-house.

(3) It is not clear whether software was used for the detection of behavior. Was position tracking software used or did blind observers individually score metrics?

We have added the information to the paper. Please see the response to Reviewer #1, Recommendations for Authors, Point #2.

(4) It is not clear why rat cages and not a true Open Field Maze were used for NOL and NOR.

We used mouse cages because in our experience that is what is ideal to detect impairments in Tg2576 mice at young ages. We think it is why we have been so successful in identifying NOL impairments in young mice. Before our work, most investigators thought behavior only became impaired later. We would like to add that, in our experience, an Open Field Maze is not the most common cage that is used.

(5) Figure 1A is not mentioned.

It had been mentioned in the Introduction. Figure B-D was the first Figure mentioned in the Results so that is why it might have been missed. We now have added it to the first section of the Results, Line 457, so it is easier to find.

6) Although Fig 7 results are somewhat complicated compared to Fig. 5 and 6 results, EEG comes chronologically earlier than NeuN and FosB expression experiments.

We have kept the order as is because as the Reviewer said, the EEG is complex. For readability, we have kept the EEG results last.

(7) Though the statistical analysis involved parametric and nonparametric tests, It is not clear which normality tests were used.

We have added the name of the normality tests in the Methods, Section E, Line 443: Tests for normality (Shapiro-Wilk) and homogeneity of variance (Bartlett’s test) were used to determine if parametric statistics could be used. We also added after this sentence clarification: When data were not normal, non-parametric data were used. When there was significant heteroscedasticity of variance, data were log transformed. If log transformation did not resolve the heteroscedasticity, non-parametric statistics were used. Because we added correlations and analysis of survival curves, we also added the following (starting on Line 451): For correlations, Pearson’s r was calculated. To compare survival curves, a Log rank (Mantel-Cox) test was performed.

Figures:

(1) In Fig. 1A, Anatomy should be placed above the line.

We changed the figure so that the word “Anatomy” is now aligned, and the arrow that was angled is no longer needed.

In Fig. 1C and 1D, the objects seem to be moved into the cage, not the mice. This schematic does not accurately reflect the Fig. 1C and 1D figure legend text.

Thank you for the excellent point. The figure has been revised. We also updated it to show the objects more accurately.

Please correct the punctuation in the Fig. 1D legend.

Thank you for mentioning the errors. We corrected the legend.

For ease of understanding, Fig. 1C and 1D should have training and testing labeled in the figure.

Thank you for the suggestion. We have revised the figure as suggested.

Author response image 6.

(2) In Figure 2, error bars for population stats (bar graphs) are not obvious or missing. Same for Figure 3.

We added two supplemental figures to show error bars, because adding the error bars to the existing figures made the symbols, colors, connecting lines and error bars hard to distinguish. For novel object location (Fig. 2) the error bars are shown in Supp. Fig. 2. For novel object recognition, the error bars are shown in Supplemental Fig. 3.

(3) The authors should consider a Methods figure for quantification of NeuN and deltaFOSB (expansions of Fig. 5C and Fig. 6C).

Please see Reviewer #1, Public Review Point #2.

(4) In Figure 5, A should be omitted and mentioned in the Methods/figure legend. B should be enlarged. C should be inset, zoomed-in images of the hilus, with an accompanying analysis image showing a clear reduction in NeuN intensity in low choline conditions compared to intermediate and high choline conditions. In D, X axes could delineate conditions (figure legend and color unnecessary). Figure 5C should be moved to a Methods figure.

We thank the review for the excellent suggestions. We removed A as suggested. We expanded B and included insets. We used different images to show a more obvious reduction of cells for the low choline group. We expanded the Methods schematics. The revised figure is Figure 6 and shown above in response to Reviewer 1, Public Review Point #2.

(5) In Figure 6, A should be eliminated and mentioned in the Methods/figure legend. B should be greatly expanded with higher and lower thresholds shown on subsequent panels (3x3 design).

We removed A as suggested. We expanded B as suggested. The higher and lower thresholds are shown in C. The revised figure is Figure 7 and shown above in response to Reviewer 1, Public Review Point #2.

(6) In Figure 7, A2 should be expanded vertically. A3 should be expanded both vertically and horizontally. B 1 and 2 should be increased, particularly B1 where it is difficult to see symbols. Perhaps colored symbols offset/staggered per group so that the spread per group is clearer.

We added a panel (A4) to show an expansion of A2 and A3. However, we did not see that a vertical expansion would add information so we opted not to add that. We expanded B1 as suggested but opted not to expand B2 because we did not think it would enhance clarity. The revised figure is below.

Author response image 7.

(7) Supplemental Figure 1 could possibly be combined with Figure 1 (use rounded corner rat cage schematic for continuity).

We opted not to combine figures because it would make one extremely large figure. As a result, the parts of the figure would be small and difficult to see.

(8) Supplemental Figure 2 - there does not seem to be any statistical analysis associated with A mentioned in the Results text.

We added the statistical information. It is now Supplemental Figure 4:

Author response image 8.

Mortality was high in mice treated with the low choline diet. A. Survival curves are shown for mice fed the low choline diet and mice fed the high choline diet. The mice fed the high choline diet had a significantly less severe survival curve. B. Left: A photo of a mouse after sudden unexplained death. The mouse was found in a posture consistent with death during a convulsive seizure. The area surrounded by the red box is expanded below to show the outstretched hindlimb (red arrow). Right: A photo of a mouse that did not die suddenly. The area surrounded by the box is expanded below to show that the hindlimb is not outstretched.

The revised text is in the Results, Section E, starting on Line 793:

“The reason that low choline-treated mice appeared to die in a seizure was that they were found in a specific posture in their cage which occurs when a severe seizure leads to death (Supplemental Figure 5). They were found in a prone posture with extended, rigid limbs (Supplemental Figure 5). Regardless of how the mice died, there was greater mortality in the low choline group compared to mice that had been fed the high choline diet (Log-rank (Mantel-Cox) test, Chi square 5.36, df 1, p=0.021; Supplemental Figure 5A).”

Also, why isn't intermediate choline also shown?

We do not have the data from the animals. Records of death were not kept, regrettably.

Perhaps labeling of male/female could also be done as part of this graph.

We agree this would be very interesting but do not have all sex information.

B is not very convincing, though it is understandable once one reads about posture.

We have clarified the text and figure, as well as the legend. They are above.

Are there additional animals that were seen to be in a specific posture?

There are many examples, and we added them to hopefully make it more convincing.

We also added posture in WT mice when there is a death to show how different it is.

Is there any relationship between seizures detected via EEG, as shown in Supplemental Figure 3, and death?

Several mice died during a convulsive seizure, which is the type of seizure that is shown in the Supplemental Figure.

(9) Supplemental Figure 3 seems to display an isolated case in which EEG-detected seizures correlate with increased IIEs. It is not clear whether there are additional documented cases of seizures that could be assembled into a meaningful population graph. If this data does not exist or is too much work to include in this manuscript, perhaps it can be saved for a future paper.

We have added other cases and revised the graph. This is now Supplemental Figure 4 and is shown above in response to Reviewer #1, Recommendation for Authors Point #4.

Frontal is misspelled.

We checked and our copy is not showing a misspelling. However, we are very grateful to the Reviewer for catching many errors and reading the manuscript carefully.

(10) Supplemental Figure 4 seems incomplete in that it does not include EEG data from months 4, 5, and 6 (see Fig. 7B).

We have added data for these ages to the Supplemental Figure (currently Supplemental Figure 6) as part B. In part A, which had been the original figure, only 1.2, 2, and 3 months-old mice were shown because there were insufficient numbers of each sex at other ages. However, by pooling 1.2 and 2 months (Supplemental Figure 6B1), 3 and 4 months (B2) and 5 and 6 months (B3) we could do the analysis of sex. The results are the same – we detected no sex differences.

Author response image 9.

IIS frequency was similar for each sex. A. IIS frequency was compared for females and males at 1.2 months (1), 2 months (2), and 3 months (3). Two-way ANOVA was used to analyze the effects of sex and diet. Female and male Tg2576 mice were not significantly different. B. Mice were pooled at 1.2 and 2 months (1), 3 and 4 months (2) and 5 and 6 months (3). Two-way ANOVA analyzed the effects of sex and diet. There were significant effects of diet for (1) and (2) but not (3). There were no effects of sex at any age.

(1) There were significant effects of diet (F(2,47)=46.21, p<0.0001) but not sex (F(1,47)=0.106, p=0.746). Female and male mice fed the low choline diet or high choline diet were significantly different from female and male mice fed the intermediate diet (all p<0.05, asterisk).

(2) There were significant effects of diet (F(2,32)=10.82, p=0.0003) but not sex (F(1,32)=1.05, p=0.313). Both female and male mice of the low choline group were significantly different from male mice fed the intermediate diet (both p<0.05, asterisk) but no other pairwise comparisons were significant.

(3) There were no significant differences (diet, F(2,23)=1.21, p=0.317); sex, F(1,23)=0.844, p=0.368).

The data are discussed the Results, Section G, tarting on Line 843:

In Supplemental Figure 6B we grouped mice at 1-2 months, 3-4 months and 5-6 months so that there were sufficient females and males to compare each diet. A two-way ANOVA with diet and sex as factors showed a significant effect of diet (F(2,47)=46.21; p<0.0001) at 1-2 months of age, but not sex (F1,47)=0.11, p=0.758). Post-hoc comparisons showed that the low choline group had fewer IIS than the intermediate group, and the same was true for the high choline-treated mice. Thus, female mice fed the low choline diet differed from the females (p<0.0001) and males (p<0.0001) fed the intermediate diet. Male mice that had received the low choline diet different from females (p<0.0001) and males (p<0.0001) fed the intermediate diet. Female mice fed the high choline diet different from females (p=0.002) and males (p<0.0001) fed the intermediate diet, and males fed the high choline diet difference from females (p<0.0001) and males (p<0.0001) fed the intermediate diet.

For the 3-4 months-old mice there was also a significant effect of diet (F(2,32)=10.82, p=0.0003) but not sex (F(1,32)=1.05, p=0.313). Post-hoc tests showed that low choline females were different from males fed the intermediate diet (p=0.007), and low choline males were also significantly different from males that had received the intermediate diet (p=0.006). There were no significant effects of diet (F(2,23)=1.21, p=0.317) or sex (F(1,23)=0.84, p=0.368) at 5-6 months of age.

Author response:

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

We are pleased that Reviewer 3 has deemed our revisions satisfactory; below, we provide responses to the remaining Recommendations for the Authors from Reviewer 2.

Reviewer #2 (Recommendations For The Authors):

Minor corrections:

• Line 91: GWT should be GNWT

Fixed, thank you.

• Figure 2: fix the label "Participationcoefficient rank" (no space between Participation and coefficient)

Fixed, thank you for spotting.

• Line 317: Figure 2 should be Figure 3

Fixed, thank you.

• Line 360: Figure 4D, right?

Fixed, thank you. We also confirm that Figure 4 and its caption are correct. Under anaesthesia, many regions have more Integrated Information than during Recovery (red regions), but the only changes that are consistently observed across all three contrasts are the decreases.

• Line 375: Should be Figure 5A

Fixed, thank you.

• The recovery period of the anesthesia data is not described in Methods.

We have now added the missing information:

“Propofol was discontinued following the deep anaesthesia scan, and participants reached level 2 of the Ramsey scale approximately 11 minutes afterwards, as indicated by clear and rapid responses to verbal commands. This corresponds to the “recovery” period 176.”

We have also expanded our discussion on the interaction between information decomposition and measures of directionality:

“Indeed, transfer entropy can itself be decomposed into information-dynamic atoms through Partial Information Decomposition and Integrated Information Decomposition 33,34,49,151; ΦID can further decompose the Normalised Directed Transfer Entropy measure used by Deco et al 5, as recently demonstrated 152. We look forward to a more refined conceptualization of the synergistic workspace architecture that takes into account both information types and the directionality of information flow – especially in datasets with higher temporal resolution.”

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In their manuscript, Yu et al. describe the chemotactic gradient formation for CCL5 bound to - i.e. released from - glycosaminoglycans. The authors provide evidence for phase separation as the driving mechanism behind chemotactic gradient formation. A conclusion towards a general principle behind the finding cannot be drawn since the work focuses on one chemokine only, which is particularly prone to glycan-induced oligomerisation.

Strengths:

The principle of phase separation as a driving force behind and thus as an analytical tool for investigating protein interactions with strongly charged biomolecules was originally introduced for protein-nucleic acid interactions. Yu et al. have applied this in their work for the first time for chemokine-heparan sulfate interactions. This opens a novel way to investigate chemokine-glycosaminoglycan interactions in general.

Response: Thanks for the encouragement of the reviewer.

Weaknesses:

As mentioned above, one of the weaknesses of the current work is the exemplification of the phase separation principle by applying it only to CCL5-heparan sulfate interactions. CCL5 is known to form higher oligomers/aggregates in the presence of glycosaminoglycans, much more than other chemokines. It would therefore have been very interesting to see, if similar results in vitro, in situ, and in vivo could have been obtained by other chemokines of the same class (e.g. CCL2) or another class (like CXCL8).

Response: We share the reviewer’s opinion that to investigate more molecules/cytokines that interact with heparan sulfate in the system should be of interesting. We expect that researchers in the field will adapt the concept to continue the studies on additional molecules. Nevertheless, our earlier study has demonstrated that bFGF was enriched to its receptor and triggered signaling transduction through phase separation with heparan sulfate (PMID: 35236856; doi: 10.1038/s41467-022-28765-z), which supports the concept that phase separation with heparan sulfate on the cell surface may be a common mechanism for heparan sulfate binding proteins. The comment of the reviewer that phase separation is related to oligomerization is demonstrated in (Figure 1—figure supplement 2C and D), showing that the more easily aggregated mutant, A22K-CCL5, does not undergo phase separation.

In addition, the authors have used variously labelled CCL5 (like with the organic dye Cy3 or with EGFP) for various reasons (detection and immobilisation). In the view of this reviewer, it would have been necessary to show that all the labelled chemokines yield identical/similar molecular characteristics as the unlabelled wildtype chemokine (such as heparan sulfate binding and chemotaxis). It is well known that labelling proteins either by chemical tags or by fusion to GFPs can lead to manifestly different molecular and functional characteristics.

Response: We agree with the reviewer that labeling may lead to altered property of a protein, thus, we have compared chemotactic activity of CCL5 and CCL5-EGFP (Figure 2—figure supplement 1). To further verify this, we performed additional experiment to compare chemotactic activity between CCL5 and Cy3-CCL5 (see Author response image 1). For the convenience of readers, we have combined the original Figure 2—figure supplement 1 with the new data (Figure R1), which replaced original Figure 2—figure supplement 1.

Author response image 1.

Chemotactic function of CCL5-EGFP and CCL5-Cy3. Cy3-Labeled CCL5 has similar activity as CCL5, 50 nM CCL5 or CCL5-Cy3 were added to the lower chamber of the Transwell. THP-1 cells were added to upper chambers. Data are mean ± s.d. n=3. P values were determined by unpaired two-tailed t-tests. NS, Not Significant.

Reviewer #2 (Public Review):

Although the study by Xiaolin Yu et al is largely limited to in vitro data, the results of this study convincingly improve our current understanding of leukocyte migration.

(1) The conclusions of the paper are mostly supported by the data although some clarification is warranted concerning the exact CCL5 forms (without or with a fluorescent label or His-tag) and amounts/concentrations that were used in the individual experiments. This is important since it is known that modification of CCL5 at the N-terminus affects the interactions of CCL5 with the GPCRs CCR1, CCR3, and CCR5 and random labeling using monosuccinimidyl esters (as done by the authors with Cy-3) is targeting lysines. Since lysines are important for the GAG-binding properties of CCL5, knowledge of the number and location of the Cy-3 labels on CCL5 is important information for the interpretation of the experimental results with the fluorescently labeled CCL5. Was the His-tag attached to the N- or C-terminus of CCL5? Indicate this for each individual experiment and consider/discuss also potential effects of the modifications on CCL5 in the results and discussion sections.

Response: We agree with the reviewer that labeling may lead to altered property of a protein, thus, we have compared chemotactic activity of CCL5 and CCL5-EGFP (Figure 2—figure supplement 1). To further verify this, we performed additional experiment to compare chemotactic activity between CCL5 and Cy3-CCL5 (see Author response image 1). For the convenience of readers, we have combined the original Figure 2—figure supplement 1 with the new data (Author response image 1), which replaced original Figure 2—figure supplement 1.

The His-tag is attached to the C-terminus of CCL5, in consideration of the potential impact on the N-terminus.

(2) In general, the authors appear to use high concentrations of CCL5 in their experiments. The reason for this is not clear. Is it because of the effects of the labels on the activity of the protein? In most biological tests (e.g. chemotaxis assays), unmodified CCL5 is active already at low nM concentrations.

Response: We agree with the reviewer that the CCL5 concentrations used in our experiments were higher than reported chemotaxis assays and also higher than physiological levels in normal human plasma. In fact, we have performed experiments with lower concentration of CCL5, where the effect of LLPS was not seen though the chemotactic activity of the cytokine was detected. Thus, LLPS-associated chemotactic activity may represent a scenario of acute inflammatory condition when the inflammatory cytokines can increase significantly.

(3) For the statistical analyses of the results, the authors use t-tests. Was it confirmed that data follow a normal distribution prior to using the t-test? If not a non-parametric test should be used and it may affect the conclusions of some experiments.

Response: We thank the reviewer for pointing out this issue. As shown in Author response table 1, The Shapiro-Wilk normality test showed that only two control groups (CCL5 and 44AANA47-CCL5+CHO K1) in Figure 3 did not conform to the normal distribution. The error was caused by using microculture to count and calculate when there were very few cells in the microculture. For these two groups, we re-counted 100 μL culture medium to calculate the number of cells. The results were consistent with the positive distribution and significantly different from the experimental group (Author response image 3). The original data for the number of cells chemoattractant by 500 nM CCL5 was revised from 0, 247, 247 to 247, 123, 370 and 500 nM 44AANA47 +CHO-K1 was revised from 1111, 1111, 98 to 740, 494, 617. The revised data does not affect the conclusion.

Author response table 1.

Table R1 Shapiro-Wilk test results of statistical data in the manuscript

Author response image 3.

Quantification of THP-1collected from the lower chamber. Data are mean ± s.d. n=3. P values were determined by unpaired two-tailed t-tests.

Recommendations for the authors:

Reviewer #1:

See the weaknesses section of the Public Review. In addition, the authors should discuss the X-ray structure of CCL5 in complex with a heparin disaccharide in comparison with their docked structure of CCL5 and a heparin tetrasaccharide.

Response: Our study, in fact, is strongly influenced by the report (Shaw, Johnson et al., 2004) that heparin disaccharide interaction with CCL5, which is highlighted in the text (page5, line100-102).

Reviewer #2:

(1) Clearly indicate in the results section and figure legends (also for the supplementary figures) which form and concentration of CCL5 is used.

Response: The relevant missing information is indicated across the manuscript.

(2) Clearly indicate which GAG was used. Was it heparin or heparan sulfate and what was the length (e.g. average molecular mass if known) or source (company?)?

Response: Relevant information is added in the section “Materials and Methods.

(3) Line 181: What do you mean exactly with "tiny amounts"?

Response: “tiny amounts” means 400 transfected cells. This is described in the section of Materials and Methods. It is now also indicated in the text and legend to the figure.

(4) Lines 216-217: This is a very general statement without a link to the presented data. No combination of chemokines is used, in vivo testing is limited (and I agree very difficult). You may consider deleting this sentence (certainly as an opening sentence for the Discussion).

Response: We appreciate very much for the thoughtful suggestion of the reviewer. This sentence is deleted in the revised manuscript.

(5) Why was 5h used for the in vitro chemotaxis assay? This is extremely long for an assay with THP-1 cells.

Response: We apologize for the unclear description. The 5 hr includes 1 hr pre- incubation of CCL5 with the cells enable to form phase separation. After transferring the cells into the upper chamber, the actual chemotactic assay was 4 hr. This is clarified in the Materials and Methods section and the legend to each figure.

(6) Define "Sec" in Sec-CCL5-EGFP and "Dil" in the legend of Figure 4.

Response: The Sec-CCL5-EGFP should be “CCL5-EGFP’’, which has now been corrected. Dil is a cell membrane red fluorescent probe, which is now defined.

(7) Why are different cell concentrations used in the experiment described in Figure 5?

Response: The samples were from three volunteers who exhibited substantially different concentrations of cells in the blood. The experiment was designed using same amount of blood, so we did not normalize the number of the cell used for the experiment. Regardless of the difference in cell numbers, all three samples showed the same trend.

(8) Check the text for some typos: examples are on line 83 "ratio of CCL5"; line 142 "established cell lines"; line 196 "peripheral blood mononuclear cells"; line 224 "to mediate"; line 226 "bind"; line 247 "to form a gradient"; line 248 "of the glycocalyx"; line 343 and 346 "tetrasaccharide"; line 409-410 "wild-type"; line 543 "on the surface of CHO-K1 and CHO-677"; line 568 "white".

Response: Thanks for the careful reading. The typo errors are corrected and Manuscript was carefully read by colleagues.

Author response:

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

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Pg. 3 - lines 51-53: "Once established, the canonical RdDM pathway takes over, whereby small RNAs are generated by the plant-specific polymerase IV (Pol IV). In both cases, a second plant-specific polymerase, Pol V, is an essential downstream component." The authors' intro omits an important aspect of Pol V's function in RdDM, which is quite relevant to their study. Pol V transcribes DNA to synthesize noncoding RNA scaffolds, to which AGO4-bound 24 nt siRNAs are thought to base pair, leading to DRM2 recruitment for cytosine methylation near to these nascent Pol V transcripts (Wierzbicki et al 2008 Cell; Wierzbicki et al. 2009 Nat Genet). I recommend that the authors cite these key studies.

These citations have now been added (see line 57).

The authors provide compelling evidence that Pol V redistributes to ectopic heterochromatin regions in h1 mutants (e.g., Fig1a browser shot). Presumably, this would allow Pol V to transcribe these regions in h1 mutants, whereas it could not transcribe them in WT plants. Have the authors detected and/or quantified Pol V transcripts in the h1 mutant compared to WT plants at the sites of Pol V redistribution (detected via NRPE1 ChIP)?

Robust detection of Pol V transcripts can be experimentally challenging, and instead we quantify and detect NRPE1 dependent methylation at these regions (Fig 5), which occurs downstream of Pol V transcript production. However, we note detecting Pol V transcripts as a potential future direction in the discussion (see line 263).

Pg. 5 - lines 101-102: Figure 1e - "The preferential enrichment of NRPE1 in h1 was more pronounced at TEs that overlapped with heterochromatin associated mark, H3K9me2 (Fig. 1e). Was a statistical test performed to determine that the overall differences are significant only at TE sites with H3K9me2? Can the sites without H3K9me2 also be differentiated statistically?

Yes, there is a statistically significant difference between WT and h1 at both the H3K9me2 marked and unmarked TEs (Wilcoxon rank sum tests, see updated Fig 1e). The size of the effect is larger for the H3K9me2 marked TEs (median difference of 0.41 vs 0.16). Median values have now been added to the boxplots so that this is directly viewable to the reader (Fig 1e). This reflects the general increase in NRPE1 occupancy in h1 mutants through the genome, with the effect consistently stronger in heterochromatin. In our initial version of the manuscript, we summarise the effect as follows “We found that h1 antagonizes NRPE1 occupancy throughout the genome, particularly at heterochromatic regions” (previous version line 83, current version line 95). Although important exceptions exist (see Fig 5, NRPE1 and DNA methylation loss in h1), we now make this point even more explicit, and have updated the manuscript at several locations (abstract line 26, results line 245, discussion line 265).

Pg. 5 - lines 108-110: The authors state, "Importantly, we found no evidence for increased NRPE1 expression at the mRNA or protein level in the h1 mutant (Suppl. Fig. 2)." But the authors did observe reduced NRPE1 transcript levels in h1 mutants, in their re-analysis of RNA-seq data and reduced NRPE1 protein signals via western blot in (Suppl. Fig. 2), which should be reported here in the results.

As described further below, we reanalysed h1 RNA-seq from scratch, and see no evidence for significant differential gene expression of NRPE1. This table and analysis are now provided in Supplementary Table 1.

More importantly, the above logic about NRPE1 expression in h1 mutants assumes that NRPE1 is the stoichiometrically limiting subunit for Pol V assembly and function in vivo, but this is not known to be the case:

(1) While NRPE1's expression is somewhat reduced (and not increased) in h1 mutant plants, we cannot be certain that other genes influencing Pol V stability or recruitment are unaffected by h1 mutants. I thus recommend that the authors perform RT-qPCR directly on the WT and h1 mutant materials used in their current study, quantifying NRPE1, NRPE2, NRPE5, DRD1, DMS3, RDM1, SUVH2 and SUVH9 transcript levels.

(2) Normalizations used to compare samples should be included with RT-qPCR and western assays. An appropriate house-keeping gene like Actin2 or Ubiquitin could be used to normalize the RT-qPCR. Protein sample loading in Suppl. Fig. 2 could be checked by Coomassie staining and/or an antibody detection of a house-keeping protein.

We have now included a full re-analysis of h1 RNA-seq (data from Choi et al 2020) focusing on transcriptional changes of DNA methylation machinery genes in the h1 mutant. Of the 61 genes analysed, only AGO6 and AGO9 were found to be differentially expressed (2-3 fold upregulation). This analysis is now included as a table

(Supplementary Table 1). The western blot has been moved to Supplementary Fig 3 to now illustrate antibody specificity and H1 loss in the h1 mutant lines, so NRPE1 itself serves as a loading control (Supplementary Fig 3a).

Pg. 6 - lines 129-131: The authors state that "over NRPE1 defined peaks (where NRPE1 occupancy is strongest in WT) we observed no change in H1 occupancy in nrpe1 (Fig 2b). The results indicate that H1 does not invade RdDM regions in the nrpe1 mutant background." This conclusion assumes that the author's H1 ChIP is successfully detecting H1 occupancy. However, in Fig 2d there does not appear to be H1 enrichment or peaks as visualized across the 10766 ZF-DMS3 off-target loci, or even at the selected 451 ZFDMS3 off-target hyper DMRs, where the putative signal for H1 enrichment on the metaplot center is extremely weak/non-existent.

As a reference for H1 enrichment in chromatin (e.g., looking where H2A.W antagonizes H1 occupancy) one can compare analyses in Bourguet et al (2021) Nat Commun, involving co-authors of the current study. Bourguet et al (2021) Fig 5b show a metaplot of H1 levels centered on H2A.W peaks with H1 ChIP signal clearly tapering away from the metaplot center point peak. To my eye, the H1 ChIP metaplots for ZF-DMS3 offtarget loci in the current manuscript (Fig 2d) resemble "shuffled peaks" controls like those in Fig 5b of Bourguet et al (2021).

Can one definitively interpret Fig 2d as showing RdDM "not reciprocally affecting H1 localization" without first showing the specificity of the ChIP-seq results in a genotype where H1 occupancy changes? Alternatively, could this dataset be displayed with Deeptools heatmaps to strengthen the evidence that the authors are detecting H1 occupancy/enrichment genome-wide, before diving into WT/nrpe1 mutant analysis at ZF-DMS3 off-target loci?

This is an excellent suggestion from the reviewer. We have now included several analyses that assess and demonstrate the quality of our H1 ChIP-seq profiles. First, as suggested by the reviewer, we show that our H1 profiles peak over H2A.W enriched euchromatic TEs as defined by Bourguet et al, mirroring these published findings. Next, we investigated whether our H1 profiles match Teano’s recently described pattern over genes, confirming a similar pattern with 3’ enrichment of H1 over H3K27me3 unmarked genes. Furthermore, we show that the H1 peaks defined here are similarly enriched with GFP tagged H1.2 from the Teano et al. 2023 study. These analyses that validate the quality of our H1 ChIP-seq datasets and bolster the conclusion that NRPE1 redistribution does not affect H1 occupancy. These new analysis are now presented in Supplementary Figure 3 and see line 153.

Pg. 8 - lines 228-230: The authors state that, "As with NRPE1, SUVH1 increased in the h1 background significantly more in heterochromatin, with preferential enrichment over long TEs, cmt2 dependent hypo CHH DMRs, and heterochromatic TEs (Fig. 6b)."

Contrary to the above statement, the violin plots in Fig. 6c show SUVH1 occupancy increasing at euchromatic TEs in the h1 mutant. What statistical test allowed the authors to determine that the increase in h1 occurs "significantly more in heterochromatin"? The authors should critically interpret Fig. 6c and 6d, which are not currently referenced in the results section. More support is needed for the claim that SUVH1 specifically encroaches into heterochromatin in the h1 mutant, rather than just TEs generally (euchromatic and heterochromatic alike).

Similar to what we see for NRPE1, statistical tests that we have now performed show that SUVH1 is significantly enriched in h1 in all classes. Importantly however, the effect size is larger in all of the heterochromatin associated classes. We display these statistical tests and the median values on the plots so that effects are immediately viewable (see updated Fig 6).

In addition, the authors should verify that SUVH1-3xFLAG transgenes (in the WT and h1 mutant backgrounds, respectively) and endogenous Arabidopsis genes encoding the transcriptional activator complex (SUVH1-SUVH3-DNAJ1-DNAJ2) are not overexpressed in the h1 mutant vs. WT. Higher expression of SUVH1 or limiting factors in the larger complex could explain the observation of increased SUVH1 occupancy in the h1 background.

We do not see a difference in SUVH1/3/DNAJ1/2 complex gene expression in the h1 background (see Supplementary Table 1). However, we cannot rule out that that our SUVH1-FLAG line in h1 is more highly expressed than the corresponding SUVH1-FLAG line in WT. We now note this point in line 248.

Pg. 8 - lines 231-232: Here the authors make a sweeping conclusion about H1 demarcating, "the boundary between euchromatic and heterochromatic methylation pathways, likely through promoting nucleosome compaction and restricting heterochromatin access." I do not see how a H1 boundary between euchromatic and heterochromatic methylation pathways is revealed based on the SUVH1-3xFLAG occupancy data, which shows increased enrichment at every category interrogated in the h1 mutant (Fig 6b,c,d) and all along the baseline too in the h1 mutant browser tracks (Fig 6a). Can the authors provide more examples of this phenomenon (similar to Fig 6a) and better explain why their SUVH1-3xFLAG ChIP supports this demarcation model?

The general conclusion from SUVH1 about H1’s agnostic role in preventing heterochromatin access is now further supported from our findings with H3K27me3 (see Figure 6e and description from line 250). However, we agree that the demarcation model as initially presented was overly simplistic. This point was also raised by reviewer 2. We have removed the line highlighted by the reviewer in the revised version of the manuscript. In the revised version we clarify that H1 impedes RdDM and associated machinery throughout the genome (consistent with H1’s established broad occupancy across the genome) but this effect is most pronounced in heterochromatin, corresponding to maximal H1 occupancy (abstract line 26, results line 245, discussion line 265). 

Corrections:

Pg. 8 - lines 226-227: "We therefore wondered whether complex's occupancy might also be affected by H1." The sentence contains a typo, where I assume the authors mean to refer to occupancy by the SUVH1-SUVH3-DNAJ1-DNAJ2 transcriptional activator complex. This needs to be specified more clearly.

The paragraph has been updated (see from line 237).

Pg. 13 - lines 393-405: There are minor errors in the capitalization of titles and author initials in the References. I recommend that the authors proofread all the references to eliminate these issues:

Thank you, these have been corrected.

Choi J, Lyons DB, Zilberman D. 2021. Histone H1 prevents non-cg methylation-mediated small RNA biogenesis in arabidopsis heterochromatin. Elife 10:1-24. doi:10.7554/eLife.72676 (...)

Du J, Johnson LM, Groth M, Feng S, Hale CJ, Li S, Vashisht A a., Gallego-Bartolome J, Wohlschlegel J a., Patel DJ, Jacobsen SE. 2014. Mechanism of DNA methylation-directed histone methylation by KRYPTONITE. Mol Cell 55:495-504. doi:10.1016/j.molcel.2014.06.009 (...)

Du J, Zhong X, Bernatavichute Y V, Stroud H, Feng S, Caro E, Vashisht A a, Terragni J, Chin HG, Tu A, Hetzel J, Wohlschlegel J a, Pradhan S, Patel DJ, Jacobsen SE. 2012. Dual binding of chromomethylase domains to H3K9me2-containing nucleosomes directs DNA methylation in plants. Cell 151:167-80. doi:10.1016/j.cell.2012.07.034

Reviewer #2 (Recommendations For The Authors):

As for a normal review, here are our major and minor points.

Major:

(1) Lines 38 to 45 of the introduction are important for the subsequent definition of heterochromatic and non-heterochromatic transposons, but the definition is ambiguous. Is heterochromatin defined by surrounding context such as pericentromeric position or is this an autonomous definition? Can a TE with the chromosomal arms be considered heterochromatic provided that it is long enough and recruits the right machinery? These cases should be more explicitly introduced. Ideally, a supplemental dataset should provide a key to the categories, genomic locations and overlapping TEs as they were used in this analysis, even if some of the categories were taken from another study.

We have now added all the regions used for analysis in this study to Supplementary Table 3.

(2) Line 80: This would be the first chance to cite Teno et al. and the "encroachment" of

PcG complexes to TEs in H1 mutants

Done - “H1 also plays a key role in shaping nuclear architecture and preventing ectopic polycomb-mediated H3K27me3 deposition in telomeres (Teano et al., 2023).” See line 83

(3) It is "only" a supplemental figure but S2 but it should still follow the rules: Indicate the number of biological replicates for the RNA-seq data, and perform a statistical test. In case of WB data, provide a loading control.

We are now using the western blot to illustrate antibody specificity and H1 loss in the h1 mutant lines, so NRPE1 itself serves as a loading control (Supplementary Fig 3a). For NRPE1 mRNA expression, we have now replaced this with a more comprehensive transcriptome analysis of methylation machinery in h1 (see Supplementary Table 1). 

(4) Lines 115 to 124 and corresponding data: Here, the goal is to exclude other changes to heterochromatin structure other than "increased access" in H1 mutants; however, only one feature, H3K9me2, is tested. Testing this one mark does not necessarily prove that the nature of the chromatin does not change, e.g. H2A.W could be differently redistributed, DDM1 may change, VIM protein, and others. Either more comprehensive testing for heterochromatin markers should be performed, or the conclusions moderated.

We have moderated the text accordingly (see line 135).

(5) Lines 166ff and Figure 1, a bit out of order also Figure 5: The general hypothesis is that NRPE1 redistributes to heterochromatic regions in h1 mutants (as do other chromatin modifiers), but the data seem to only support a higher occurrence at target sites.

a. The way the NRPE1 data is displayed makes it seem like there is much more NRPE1 in the h1 samples, even at peaks that should not be recruiting more as they do not represent "long" TEs. It would be good to present more gbrowse shots of all peak classes.

We now clarify that h1 does result in a general increase of NRPE1 throughout the genome, but the effect is strongest at heterochromatin. In our initial version of the manuscript, we summarise the effect as follows “We found that h1 antagonizes NRPE1 occupancy throughout the genome, particularly at heterochromatic regions” (previous version line 83, current version line 95). We have modified the language at several locations throughout the manuscript to make this point more clearly (abstract line 26, results line 245, discussion line 265). We include several browser shots in Supp Fig. 8.

b. The data are "normalized" how exactly?

c. One argument of observing "gaining" and "losing" peaks is that there is redistribution of NRPE1 from euchromatic to heterochromatic sites. There should be an analysis and figure to corroborate the point (e.g. by comparing FRIP values). Figure 1b shows lower NRPE1 signals at the TE flanking regions. This could reflect a redistribution or a flawed normalization procedure.

The data are normalised using a standardised pipeline by log2 fold change over input, after scaling each sample by mapped read depth using the bamCompare function in deepTools. This is now described in detail in the Materials and Methods line 365, with full code and pipelines available from GitHub (https://github.com/Zhenhuiz/H1-restrictseuchromatin-associated-methylation-pathways-from-heterochromatic-encroachment).

d. Figure 1d and f show similar profiles comparing "long" and "short" TEs or "CMT2 dependent hypo-CHH" and "DRM2 dependent CHH". How do these categories relate to each other, how many fragments are redundant?

The short vs long TEs were defined in Liu et al 2018 (doi: 10.1038/s41477-017-0100-y) and the DMRs were defined in Zhang et al. 2018 (DOI: 10.1073/pnas.1716300115). There is likely to be some degree of overlap between the categories, but numbers are very different (short TEs (n=820), long TEs (n=155), drm2 DMRs (n=5534), CMT (n=21784)) indicating that the different categories are informative. We have now listed all the regions used for analysis in this study as in Supplementary Table 3.

e. The purpose of the data presented in Figure 1 b is to compare changes of NRPE1 association in H3K9me3 non-overlapping and overlapping TEs between wild-type and background, yet the figure splits the categories in two subpanels and does neither provide a fold-change number nor a statistical test of the comparison. As before, the figure does not really support the idea that NPRE1 somehow redistribute from its "normal" sites towards heterochromatin as both TE classes seem to show higher NRPE1 binding in h1 mutants.

There is a statistically significant difference between WT and h1 at both the H3K9me2 marked and unmarked TEs, however, the size of the effect is larger for the H3K9me2 marked TEs (median difference of 0.41 vs 0.16). Median values have now been added to the boxplots so that this is directly viewable to the reader (Fig 1e). Although important exceptions exist (see Fig 5 – regions that lose NRPE1 and DNA methylation), this reflects the general increase in NRPE1 occupancy in h1 mutants throughput the genome, with a consistently stronger effect in heterochromatin. As noted above, we have updated the manuscript to make this point more clearly (abstract line 26, results line 245, discussion line 265).

f. Panel g is the only attempt to corroborate the redistribution towards heterochromatic regions, but at this scale, the apparent reduction of binding in the chromosome arms may be driven by off-peak differences and normalization problems between different ChIP samples with different signal-to-noise-ratio.

We describe our normalisation and informatic pipeline in more detail in the Materials and Methods line 365. It is also important to note that the reduction is not only observed at the chromosomal level, but also at specific sites. We called differential peaks between WT and h1 mutant. The "Regions that gain NRPE1 in h1" peaks are more enriched in heterochromatic regions, while " Regions that lose NRPE1 in h1" peaks are more enriched outside heterochromatic regions.

g. Figure 5: how many regions gain vs lose NRPE1 in h1 mutants? If the "redistribution causes loss" scenario applies, the numbers should overall be balanced but that does not seem the case. The loss case appears to be rather exceptional judging from the zigzagging meta-plot. Are these sites related to the sites taken over by PcG-mediated repression in h1 mutants?

As described in line 222 (previous version of the manuscript line 206), there are 15,075 sites that gain and 1,859 sites that lose NRPE1 in h1. Comparing these sites to

H3K27me3 in the Teano et al. study was an excellent suggestion. We compared sites that gain NRPE1 to sites that gain H3K27me3 in h1, finding a statistically significant overlap (2.4 fold enrichment over expected, hypergeometric test p-value 2.1e-71). Reciprocally, sites that lose NRPE1 were significantly enriched for overlap with H3K27me3 loss regions (1.6 fold over expected, hypergeometric test p-value 1.4e-4). This indicates that RdDM and H3K27me3 patterning are similarly modulated by H1. To directly test this, we reanalysed the H3K27me3 ChIP-seq data from Teano et al., finding coincident gain and loss of H3K27me3 at sites that gain and lose NRPE1 in h1. These results are described from line 250 and in Fig 6e, which supports a general role for H1 in preventing heterochromatin encroachment.

(6) Lines 166ff and Figure 3: The data walk towards the scenario of pathway redistribution but actually find that RdDM plays a minor role overall as a substantial increase in heterochromatin regions occurs in all contexts and is largely independent of RdDM.

a. How exactly are DNA-methylation data converted across regions to reach a fraction score from 0 to 1? There is no explanation in the legend for the methods that allow to recapitulate.

We now explain our methods in full in the Materials and Methods and all the code for generating these has now been deposited on GitHub (https://github.com/Zhenhuiz/H1restricts-euchromatin-associated-methylation-pathways-from-heterochromaticencroachment). Briefly, BSMAP is used to calculate the number of reads that are methylated vs unmethylated on a per-cytosine basis across the genome. Next, the DNA methylation fraction in each region is calculated by adding all the methylation fractions per cytosine in a given window, and divided by the total number of cytosines in that same window (ie mC/(unmC+mC)) i.e. this is expressed as a fraction ranging from 0 to 1.

“0” indicates this region is not methylated, and “1” indicates this region is fully methylated (every cytosine is 100% methylated).  

b. Kernel plots? These are slang for experts and should be better described. In addition, nothing is really concluded from these plots in the text, although they may be quite informative.

Kernel density plots show the proportion of TEs that gain or lose methylation in a particular mutant, rather than the overall average as depicted in the methylation metaplots above. We now describe the kernel density plots in more detail in the Figure 3 legend. 

(7) Figure 4: This could be a very interesting analysis if the reader could actually understand it.

a. The legend is minimal. What is the meaning of hypo and hyper regions indicated to the right of Figure 4c?

b. The color scale represents observed/expected values. What exactly does this mean? Mutant vs WT?

c. Some comparisons in 4a are cryptic, e.g. h1 nrpe1 nrpe1 vs CHH?

d. Figure 4d focuses on a correlation square of relevance, but why? Interestingly the square does not correspond to any "hypo" or "hyper" label?

Thank you, we have revised Figure 4 and legend based on these suggestions to clarify all of the above.

(8) Lines 226 and Figure 6B. De novo (or increased) targeting of SUVH1 to heterochromatic sites in h1 mutants, similar to NRPE1, is used to support the argument that more access allows other chromatin modifiers to encroach. SUVH1 strongly depends on RdDM for its in vivo binding and may be the least conclusive factor to argue for a "general" encroachment mechanism.

We appreciate the reviewers point here. Something that is entirely independent of RdDM following the same pattern would be stronger evidence in favour of general encroachment. Excitingly, this is exactly what we provide evidence for when investigating the interrelationship with H3K27me3 and we appreciate the reviewer’s suggestion to check this! This data is now described in Figure 6e and line 250.

Minor:

(1) Line 23: "Loss of H1 resulted in heterochromatic TE enrichment by NRPE1." This does not seem right. NRPE enrichment as TEs

Modified, (line 26) thank you.

(2) Lines 73-74: The idea that DDM1 displaces H1 in heterochromatic TEs is somewhat counterintuitive to model that heterochromatic TEs are unavailable for RdDM because of the presence of H1. Is this displacement non-permanent and directly linked to interaction with CMT2/3 Met1?

This is a very good question and we agree with the reviewer that the effect of DDM1 may only be transient or insufficient to allow for full RdDM assembly, or indeed there may be a direct interaction between DDM1 and CMTs/MET1. During preparation of these revisions, a structure of Arabidopsis nucleosome bound DDM1 was published, which provides some insight by showing that DDM1 promotes DNA sliding. This is at least consistent with the idea of DDM1 causing transient / non-permanent displacement of H1 that would be insufficient for RdDM establishment. We incorporate discussion of these ideas at line 80.

(3) Line 85: A bit more background on the Reader activator complex should be given. In fact, the reader may not really care that it was more recently discovered (not really recent btw) but what does it actually do?

We have quite extensively reconfigured this paragraph to take into account our new finding with H3K27me3, such that there is less emphasis on the reader activator complex. The sentence now reads as follows:

“We found that h1 antagonizes NRPE1 occupancy throughout the genome, particularly at heterochromatic regions. This effect was not limited to RdDM,  similarly impacting both the methylation reader complex component, SUVH1 (Harris et al., 2018) and polycomb-mediated H3K27me3 (Teano et al., 2023).” (line 95). 

Also, when describing the experiment the results section (line 241), we now provide more background on SUVH1’s function.

(4) Lines 80-81: Since it is already shown that RdDM associated small RNAs are more enriched in h1 at heterochromatin, help us to know what is precisely the added value of studying the enrichment of NRPE1 at these sites.

Good point. We have the following line: ‘...small RNAs are not a direct readout of functional RdDM activity and Pol IV dependent small RNAs are abundant in regions of the genome that do not require RdDM for methylation maintenance and that do not contain Pol V (Stroud et al., 2014).’ (line 90)

(5) Line 99: This seems to be the only time where the connection between long TEs and heterochromatic regions is mentioned but no source is cited.

We have added the following appropriate citations: (Bourguet et al., 2021; Zemach et al., 2013). (line 110).

(6) Line 100: DMRs is used for the first time here without explanation and full text. The abbreviation is introduced later in the text (Line 187).

Thank you, we now describe DMRs upon first use, line 112.

(7) Figure 2: Panels 2 c and d should show metaplots for WT and transgenes in one panel. There is something seriously wrong with the normalization in d or the scale for left and right panel is not the same. Neither legend nor methods describe how normalization was performed.

Thank you for pointing this out, the figure has been corrected. We have updated the Materials and Methods (line 365) and have added codes and pipelines to GitHub to explain the normalisation procedure in more detail (https://github.com/Zhenhuiz/H1restricts-euchromatin-associated-methylation-pathways-from-heterochromaticencroachment).

Author response:

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

We are very grateful to the reviewers for their constructive comments. Here is a summary of the main changes we made from the previous manuscript version, based on the reviewers’ comments:

(1) Introduction of a new model, based on a Markov chain, capturing within-trial evolution in search strategy .

(2) Addition of a new figure investigating inter-animal variations in search strategy.

(3) Measurement of model fit consistency across 10 simulation repetitions, to prevent the risk of model overfitting.

(4) Several clarifications have been made in the main text (Results, Discussion, Methods) and figure legends.

(5) We now provide processed data and codes for analyses and models at GitHub repository

(6) Simplification of the previous modeling. We realized that the two first models in the previous manuscript version were simply special cases of the third model. Therefore, we retained only the third model, which has been renamed as the ‘mixture model’.

(7) Modification of Figure 4-6 and Supplementary Figure 7-8 (or their creation) to reflect the aforementioned changes

Public Reviews:

Reviewer #1 (Public Review):

The authors design an automated 24-well Barnes maze with 2 orienting cues inside the maze, then model what strategies the mice use to reach the goal location across multiple days of learning. They consider a set of models and conclude that one of these models, a combined strategy model, best explains the experimental data.

This study is written concisely and the results presented concisely. The best fit model is reasonably simple and fits the experimental data well (at least the summary measures of the data that were presented).

Major points:

(1) One combined strategy (once the goal location is learned) that might seem to be reasonable would be that the animal knows roughly where the goal is, but not exactly where, so it first uses a spatial strategy just to get to the first vestibule, then switches to a serial strategy until it reaches the correct vestibule. How well would such a strategy explain the data for the later sessions? The best combined model presented in the manuscript is one in which the animal starts with a roughly 50-50 chance of a serial (or spatial strategy) from the start vestibule (i.e. by the last session before the reversal the serial and spatial strategies are at ~50-50m in Fig. 5d). Is it the case that even after 15 days of training the animal starts with a serial strategy from its starting point approximately half of the time? The broader point is whether additional examination of the choices made by the animal, combined with consideration of a larger range of possible models, would be able to provide additional insight into the learning and strategies the animal uses.

Our analysis focused on the evolution of navigation strategies across days and trials. The reviewer raises the interesting possibility that navigation strategy might evolve in a specific manner within each trial, especially on the later days once the environment is learned. To address this possibility, we first examined how some of the statistical distributions, previously analyzed across days, evolved within trials. Consistent with the reviewer’s intuition, the statistical distributions changed within trials, suggesting a specific strategy evolution within trials. Second, we developed a new model, where strategies are represented as nodes of a Markov chain. This model allows potential strategy changes after each vestibule visit, according to a specific set of transition probabilities. Vestibules are chosen based on the same stochastic processes as in the previous model. This new model could be fitted to the experimental distributions and captured both the within-trial evolution and the global distributions. Interestingly, the trials were mostly initiated in the random strategy (~67% chance) and to a lesser extent in the spatial strategy (~25% chance), but rarely in the serial strategy (~8% chance). This new model is presented in Figure 6.

(2) To clarify, in the Fig. 4 simulations, is the "last" vestibule visit of each trial, which is by definition 0, not counted in the plots of Fig. 4b? Otherwise, I would expect that vestibule 0 is overrepresented because a trial always ends with Vi = 0.

The last vestibule visit (vestibule 0 by definition) is counted in the plots of Fig.4b. We initially shared the same concern as the reviewer. However, upon further consideration, we arrived at the following explanation: A factor that might lead to an overrepresentation of vestibule 0 is the fact that, unlike other vestibules, it has to be contained in each trial, as trials terminated upon the selection of vestibule 0. Conversely, a factor that might contribute to an underrepresentation of vestibule 0 is that, unlike other vestibules, it cannot be counted more than once per trial. Somehow these two factors seem to counterbalance each other, resulting in no discernible overrepresentation or underrepresentation of vestibule 0 in the random process. 

Reviewer #2 (Public Review):

This paper uses a novel maze design to explore mouse navigation behaviour in an automated analogue of the Barnes maze. Overall I find the work to be solid, with the cleverly designed maze/protocol to be its major strength - however there are some issues that I believe should be addressed and clarified.

(1) Whilst I'm generally a fan of the experimental protocol, the design means that internal odor cues on the maze change from trial to trial, along with cues external to the maze such as the sounds and visual features of the recording room, ultimately making it hard for the mice to use a completely allocentric spatial 'place' strategy to navigate. I do not think there is a way to control for these conflicts between reference frames in the statistical modelling, but I do think these issues should be addressed in the discussion.

It should be pointed out that all cues on the maze (visual, tactile, odorant) remained unchanged across trials, since the maze was rotated together with goal and guiding cues. Furthermore, the maze was equipped with an opaque cover to prevent mice from seeing the surrounding room (the imaging of mouse trajectories was achieved using infrared light and camera). It is however possible that some other cues such as room sounds and odors could be perceived and somewhat interfered with the sensory cues provided inside the maze. We have now mentioned this possibility in the discussion.

(2) Somewhat related - I could not find how the internal maze cues are moved for each trial to demarcate the new goal (i.e. the luminous cues) ? This should be clarified in the methods.

The luminous cues were fixed to the floor of the arena. Consequently, they rotated along with the arena as a unified unit, depicted in figure 1. We have added some clarifications in Figure 1 legend and methods.

(3) It appears some data is being withheld from Figures 2&3? E.g. Days 3/4 from Fig 2b-f and Days 1-5 on for Fig 3. Similarly, Trials 2-7 are excluded from Fig 3. If this is the case, why? It should be clarified in the main text and Figure captions, preferably with equivalent plots presenting all the data in the supplement.

The statistical distributions for all single days/trials are shown in the color-coded panels of Figure2&3. In the line plots of Figure2&3, we show only the overlay of 2-3 lines for the sake of clarity. The days/trials represented were chosen to capture the dynamic range of variability within the distributions. We have added this information in the figure legends.

(4) I strongly believe the data and code should be made freely available rather than "upon reasonable request".

Matrices of processed data and various codes for simulations and analyses are now available at https://github.com/ sebiroyerlab/Vestibule_sequences.

Reviewer #3 (Public Review):

Royer et al. present a fully automated variant of the Barnes maze to reduce experimenter interference and ensure consistency across trials and subjects. They train mice in this maze over several days and analyze the progression of mouse search strategies during the course of the training. By fitting models involving stochastic processes, they demonstrate that a model combined of the random, spatial, and serial processes can best account for the observed changes in mice's search patterns. Their findings suggest that across training days the spatial strategy (using local landmarks) was progressively employed, mostly at the expense of the random strategy, while the serial strategy (consecutive nearby vestibule check) is reinforced from the early stages of training. Finally, they discuss potential mechanistic underpinnings within brain systems that could explain such behavioral adaptation and flexibility.

Strength:

The development of an automated Barnes maze allows for more naturalistic and uninterrupted behavior, facilitating the study of spatial learning and memory, as well as the analysis of the brain's neural networks during behavior when combined with neurophysiological techniques. The system's design has been thoughtfully considered, encompassing numerous intricate details. These details include the incorporation of flexible options for selecting start, goal, and proximal landmark positions, the inclusion of a rotating platform to prevent the accumulation of olfactory cues, and careful attention given to atomization, taking into account specific considerations such as the rotation of the maze without causing wire shortage or breakage. When combined with neurophysiological manipulations or recordings, the system provides a powerful tool for studying spatial navigation system.

The behavioral experiment protocols, along with the analysis of animal behavior, are conducted with care, and the development of behavioral modeling to capture the animal's search strategy is thoughtfully executed. It is intriguing to observe how the integration of these innovative stochastic models can elucidate the evolution of mice's search strategy within a variant of the Barnes maze.

Weakness:

(1) The development of the well-thought-out automated Barnes maze may attract the interest of researchers exploring spatial learning and memory. However, this aspect of the paper lacks significance due to insufficient coverage of the materials and methods required for readers to replicate the behavioral methodology for their own research inquiries.

Moreover, as discussed by the authors, the methodology favors specialists who utilize wired recordings or manipulations (e.g. optogenetics) in awake, behaving rodents. However, it remains unclear how the current maze design, which involves trapping mice in start and goal positions and incorporating angled vestibules resulting in the addition of numerous corners, can be effectively adapted for animals with wired implants.

The reviewer is correct in pointing out that the current maze design is not suitable for performing experiments with wired implant, particularly due to the maze’s enclosed structure and the access to the start/goal boxes through side holes. Instead, pharmacogenetics and wireless approaches for optogenetic and electrophysiology would need to be used. We have now mentioned this limitation in the discussion.

(2) Novelty: In its current format, the main axis of the paper falls on the analysis of animal behavior and the development of behavioral modeling. In this respect, while it is interesting to see how thoughtfully designed models can explain the evolution of mice search strategy in a maze, the conclusions offer limited novel findings that align with the existing body of research and prior predictions.

We agree with the reviewer that our study is weakly connected to previous researches on hippocampus and spatial navigation, as it consists mainly of animal behavior analysis and modeling and addresses a relatively unexplored topic. We hope that the combination of our behavioral approach with optogenetic and electrophysiology will allow in the future new insights that are in line with the existing body of research.

(3) Scalability and accessibility: While the approach may be intriguing to experts who have an interest in or are familiar with the Barnes maze, its presentation seems to primarily target this specific audience. Therefore, there is a lack of clarity and discussion regarding the scalability of behavioral modeling to experiments involving other search strategies (such as sequence or episodic learning), other animal models, or the potential for translational applications. The scalability of the method would greatly benefit a broader scientific community. In line with this view, the paper's conclusions heavily rely on the development of new models using custom-made codes. Therefore, it would be advantageous to make these codes readily available, and if possible, provide access to the processed data as well. This could enhance comprehension and enable a larger audience to benefit from the methodology.

The current approach might indeed extend to other species in equivalent environments and might also constitute a general proof of principle regarding the characterization of animal behaviors by the mixing of stochastic processes. We have now mentioned these points in the discussion.

As suggest by the reviewer, we have now provided model/simulation codes and processed data to replicate the figures, at https://github.com/sebiroyerlab/Vestibule_sequences

(4) Cross-validation of models: The authors have not implemented any measures to mitigate the risk of overfitting in their modeling. It would have been beneficial to include at least some form of cross-validation with stochastic models to address this concern. Additionally, the paper lacks the presence of analytics or measures that assess and compare the performance of the models.

To avoid the risk of model overfitting, the most appropriate solution appeared to be repeating the simulations several times and examining the consistency of the obtained parameters across repetitions. For the mixture model, we now show in Supplementary figure 7 the probabilities obtained from 10 repetitions of the simulation. Similarly, for the Markov chain model, the probabilities obtained from 10 repetitions of the simulation are shown in Figure 6.

Regarding model comparison, we have simplified our mixture model into only one model, as we realized the 2 other models in the previous manuscript version were simply special cases of the 3rd model. Nevertheless, comparison was still needed for the estimation for the best value of N (the number of consecutive segments that a strategy lasts) in the mixture model. We now show the comparison of mean square errors obtained for different values of N, using t-test across 10 repetitions of the simulations (Figure 5c).

(5) Quantification of inter-animal variations in strategy development: It is important to investigate, and address the argument concerning the possibility that not all animals recruit and develop the three processes (random, spatial, and serial) in a similar manner over days of training. It would be valuable to quantify the transition in strategy across days for each individual mouse and analyze how the population average, reflecting data from individual mice, corresponds to these findings. Currently, there is a lack of such quantification and analysis in the paper.

We have added a figure (Supplementary figure 8) showing the mixture model matching analyses for individual animals. A lot of variability is indeed observed across animals, with some animals displaying strong preferences for certain strategies compare to others. The average across mouse population showed a similar trend as the result obtained with the pooled data.

Recommendations for the authors:

Summary of Reviewer Comments:

(1) In its present form, the manuscript lacks sufficient coverage of the materials and methods necessary for readers to replicate the behavioral methodology in their own research inquiries. For instance, it would be beneficial to clarify how the cues are rotated relative to the goal.

(2) The models may be over-fitted, leading to spurious conclusions, and cross-validation is necessary to rule out this possibility.

(3) The specific choice of the three strategies used to fit behavior in this model should be better justified, as other strategies may account for the observed behavior.

(4) The study would benefit from an analysis of behavior on an animal-by-animal basis, potentially revealing individual differences in strategies.

(5) Spatial behavior is not necessarily fully allocentric in this task, as only the two cues in the arena can be used for spatial orientation, unlike odor cues on the floor and sound cues in the room. This should be discussed.

(6) Making the data and code fully open source would greatly strengthen the impact of this study.

In addition, each reviewer has raised both major and minor concerns which should be addressed if possible.

Reviewer #1 (Recommendations For The Authors):

Minor points:

(1) Change "tainted" to "tinted" in Fig. 1a

(2) Should note explicitly in Fig. 2d that the goal is at vestibule 0, and also in the legend

(3) Fig. 3 legend should say "c-e)", not "c-f)"

(4) Supplementary Fig. 8 legend repeats "d)" twice

Reviewer #2 (Recommendations For The Authors):

Packard & McGaugh 1996 is cited twice as refs 5 and 14

Reviewer #3 (Recommendations For The Authors):

- Figure 3: Please correct the labels referenced as "c-f)" in the figure's legend.

- Rounding numbers issue on page 4: 82.62% + 17.37% equals 99.99%, not 100%.

We fixed all minor points. We are very thankful to the reviewers for their constructive comments.

Author response:

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

We are thankful to the reviewers and the editor for their detailed feedback, insightful suggestions, and thoughtful assessment of our work. Our point-by-point responses to the comments and suggestions are below.

The revised manuscript has taken into account all the comments of the three reviewers. Modifications include corrections to errors in spelling and unit notation, additional quantification, improvements to the clarity of the language in some places, as well as additional detail in the descriptions of the methods, and revisions to the figures and figure legends.

We have also undertaken additional analyses and added materials in response to reviewer suggestions. In brief:

In response to a suggestion from Reviewer #1, we added Figure 6-1 to show examples of the calcium traces of individual fish and individual ROIs from the condensed data in Figure 6. We revised Figure 7 as follows:

• We added an analysis of the duration of the response to shock to address comments from Reviewers #2 and #3.

• In response to Reviewer #3, we added histograms showing the distribution of the amplitudes of the calcium signals in the gsc2 and rln3a neurons to show, without relying on the detection of peaks in the calcium trace, that the rln3a neurons have more oscillations in activity.

We added Figure 8-2 in response to the suggestion from Reviewer #3 to analyze turning behavior in larvae with ablated rln3a neurons.

To address Reviewer #2’s suggestion to show how the ablated transgenic animals compare to the non-ablated transgenic animals of the same genotype, we have added this analysis as Figure 8-3.

A detailed point-by-point is as follows:

The reviewers agree that the study of Spikol et al is important, with novel findings and exciting genetic tools for targeting cell types in the nucleus incertus. The conclusions are overall solid. Results could nonetheless be strengthened by performing few additional optogenetic experiments and by consolidating the analysis of calcium imaging and behavioral recordings as summarized below.

(1) Light pulses used for optogenetic-mediated connectivity mapping were very long (5s), which could lead to non specific activation of numerous population of neurons than the targeted ones. To confirm their results, the authors should repeat their experiments with brief 5-50ms (500ms maximum) -long light pulses for stimulation.

As the activity of the gsc2 neurons is already increased by 1.8 fold (± 0.28) within the first frame that the laser is activated (duration ~200 msec), it is unlikely that that the observed response is due to non-specific activation induced by the long light pulse.

(2) In terms of analysis, the authors should improve :

a) The detection of calcium events in the "calcium trace" showing the change in fluorescence over time by detecting the sharp increase in the signal when intracellular calcium rises;

We have added an additional analysis to Figure 7 that does not rely on detection of calcium peaks. See response to Reviewer #3.

b) The detection of bouts in the behavioral recordings by measuring when the tail beat starts and ends, thereby distinguishing the active swimming during bouts from the immobility observed between bouts.

Our recordings capture the entire arena that the larva can explore in the experiment and therefore lack the spatial resolution to capture and analyze the tail beat. Rather, we measured the frequency and length of phases of movement in which the larva shows no more than 1 second of immobility. To avoid confusion with studies that measure bouts from the onset of tail movement, we removed this term from the manuscript and refer to activity as phases of movement.

(3) The reviewers also ask for more precisions in the characterization of the newly-generated knock-in lines and the corresponding anatomy as explained in their detailed reports.

Please refer to the point-by-point request for additional details that have now been added to the manuscript.

Reviewer #1 (Recommendations For The Authors):

The conclusions of this paper are mostly well supported by data, but some technical aspects, especially about calcium imaging and data analysis, need to be clarified.

(1) Both the endogenous gsc2 mRNA expression and Tg(gsc2:QF2) transgenic expression are observed in a neuronal population in the NI, but also in a more sparsely distributed population of neurons located more anteriorly (for example, Fig. 2B, Fig. 5A). The latter population is not mentioned in the text. It would be necessary to clarify whether or not this anterior population is also considered as the NI, and whether this population was included for the analysis of the projection patterns and ablation experiments.

The sparsely distributed neurons had been mentioned in the Results, line 134, but we have now added more detail. In line 328, we have clarified that: “As the sparsely distributed anterior group of gsc2 neurons (Fig. 2B, C) are anatomically distinct from the main cluster and not within the nucleus incertus proper, they were excluded from subsequent analyses.”

(2) Both Tg(gsc2:QF2) and Tg(rln3a:QF2) transgenic lines have the QF genes inserted in the coding region of the targeted genes. This probably leads to knock out of the gene in the targeted allele. Can the authors mention whether or not the endogenous expression of gsc2 and rln3a was affected in the transgenic larvae? Is it possible that the results they obtained using these transgenic lines are affected by the (heterozygous or homozygous) mutation of the targeted genes?

Figure 8-1 includes in situ hybridization for gsc2 and rln3a in heterozygous Tg(gsc2:QF2)c721; Tg(QUAS:GFP)c578 and Tg(rln3a:QF2; he1.1:YFP)c836; Tg(QUAS:GFP)c578 transgenic larvae.

The expression of gsc2 is unaffected in Tg(gsc2:QF2)c721; Tg(QUAS:GFP)c578 heterozygotes

(Fig. 8-1A), whereas the expression of rln3a is reduced in Tg(rln3a:QF2; he1.1:YFP)c836; Tg(QUAS:GFP)c578 heterozygous larvae (Fig. 8-1D), as mentioned in the legend for Figure 8-1. We confirmed these findings by comparing endogenous gene expression between transgenic and non-transgenic siblings that were processed for RNA in situ hybridization in the same tube.

The behavioral results we obtained are not due to rln3a heterozygosity because comparisons were made with sibling larvae that are also heterozygous for Tg(rln3a:QF2; he1.1:YFP)c836; Tg(QUAS:GFP)c578, as stated in the Figure 8 legend.

(3) Optogenetic activation and simultaneous calcium imaging is elegantly designed using the combination of the orthogonal Gal4/UAS and QF2/QUAS systems (Fig. 6). However, I have some concerns about the analysis of calcium responses from a technical point of view. Their definition of ΔF/F in this manuscript is described as (F-Fmin)/(Fmax-Fmin) (see line 1406). This is confusing because it is different from the conventional definition of ΔF/F, which is F-F0/F0, where F0 is a baseline GCaMP fluorescence. Their way of calculating the ΔF/F is inappropriate for measuring the change in fluorescence relative to the baseline signal because it rather normalizes the amplitude of the responses across different ROIs. The same argument applies to the analyses done for Fig. 7.

We have taken a careful look at our analyses and replotted the data using F-F0/F0. However, this only changes Y-axis values and does not change the shape of the calcium trace or the change in signal upon stimulation. Both metrics (F-F0/F0 and (F-Fmin)/(Fmax-Fmin)) adjust the fluorescence values of each ROI to its own baseline.

(4) The %ΔF/F plots shown in Fig.6 are highly condensed showing the average of different ROIs (cells) within one fish and then the average of multiple fish. It would be helpful to see example calcium traces of individual ROIs and individual fish to know the variability across ROIs and fish. Also, It would be helpful to know how much laser power (561 nm laser) was used to photostimulate ReaChR.

Laser power (5%) was added to the section titled Calcium Signaling in Methods.

In Figure 6, shading in the %ΔF/F plots (D, D’, E, E’, F, F’, G, G’, H, H’) represents the variability across ROIs, and the dot plots (D’’, E’’, F’’, G’’, H’’) show the variability across fish (where each data point represents an individual fish). We have now also added Figure 6-1 with examples of calcium traces from individual fish and individual ROIs.

(5) Some calcium traces presented in Fig. 6 (Fig. 6D, D', F, H, H') show discontinuous fluctuations at the onset and offset of the photostimulation period. Is this caused by some artifacts introduced by switching the settings for the photostimulation? The authors should mention if there are some alternative explanations for this discontinuity.

As noted by the reviewer, this artifact does result from switching the settings for photostimulation, which we mention in the legend for Figure 6.

(6) In the introduction, they mention that the griseum centrale is a presumed analogue of the NI (lines 74-75). It would be helpful for the readers to better understand the brain anatomy if the authors could discuss whether or not their findings on the gsc2 and rln3a NI neurons support this idea.

Our findings on the gsc2 and rln3a neurons support the idea that the griseum centrale of fish is the analogue of the mammalian NI. We have now edited the text in the third paragraph of the discussion, line 1271, to make this point more clearly: “By labeling with QUAS-driven fluorescent reporters, we determined that the anatomical location, neurotransmitter phenotype, and hodological properties of gsc2 and rln3a neurons are consistent with NI identity, supporting the assertion that the griseum centrale of fish is analogous to the mammalian NI. Both groups of neurons are GABAergic, reside on the floor of the fourth ventricle and project to the interpeduncular nucleus.”

Reviewer #2 (Recommendations For The Authors):

Major comments:

(1) Throughout the figures a need for more precision and reference in the anatomical evidence:

• Specify how many planes over which height were projected for each Z-projection in Figure 1,2,3, ....

We added this information to the last paragraph of the section titled Confocal Imaging within the Materials and Methods.

• Provide the rhombomere numbers, deliminate the ventricles & always indicate on the panel the orientation (Rostral Caudal, Left Right or Ventral Dorsal) for Figure 1 panels D-F , Figure 2-1B-G, Figure 2-2A-C in the adult brain, Figure 3.

We annotated Figures 2-1 and 2-2 as suggested. We also indicated the orientation (anterior to the top or anterior to the left) in all figure legends. For additional context on the position of gsc2 and rln3a neurons within the larval brain, refer to Fig. 1A-C’, Fig. 1-2A, Fig. 2, Fig. 4 and Fig. 5.

• Add close up when necessary: Figure 2-2A-C, specify in the text & in the figure where are the axon bundles from the gsc2+ neurons in the adult brain- seems interesting and is not commented on?

We added a note to the legend of Figure 2-2: Arrowheads in B and B’ indicate mApple labeling of gsc2 neuronal projections to the hypothalamus. We also refer to Fig 2-2B, B’ in the Results section titled Distinct Projection Patterns of gsc2 and rln3a neurons.

• keep the same color for one transgene within one figure: example, glutamatergic neurons should always be the same color in A,B,C - it is confusing as it is.

We have followed the reviewer’s suggestion and made the color scheme consistent in Figure 3.

• Movies: add the labels (which transgenic lines in which color, orientation & anatomical boundaries for NI, PAG, any other critical region that receives their projections and the brain ventricle boundaries) on the anatomical movies in supplemental (ex Movie 4-1 for gsc2 neurons and 4-2 for rln3 neurons: add cerebellum, IPN, raphe, diencephalon, and rostral and caudal hypothalamus, medulla for 4-1 as well as lateral hypothalamus and optic tectum for 42); add the ablated region when necessary.

We added more detail to the movie legends. Please refer to Figure 4 for additional anatomical details.

• for highlighting projections from NI neurons and distinguish them from the PAG neurons, the authors elegantly used 2 Photon ablation of one versus the other cluster: this method is valid but we need more resolution that the Z stacks added in supplemental by performing substraction of before and after maps.

We are not sure what the author meant by subtraction as there are no before and after images in this experiment. Larvae underwent ablation of cell bodies and were imaged one day later in comparison to unablated larvae.

In particular, it is not clear to me if both PAG and NI rln3a neurons project to medulla - can the authors specify this point & the comparison between intact & PAG vs NI ablation maps? The authors should resolve better the projections to all targeted regions of NI gsc2 neurons and differentiate them from other PAG gsc2 neurons, same for rln3a neurons.

We have clarified this point on line 549.

Make sure to mention in the result section the duration between ablation & observation that is key for the axons to degrade.

We always assessed degeneration of neuronal processes at 1-day post-ablation.

(“2) calcium imaging experiments:

a) with optogenetic connectivity mapping:

the authors combine an impressive diverse set of optogenetic actuators & sensors by taking advantage of the QUAS/QF2 and UAS/GAL4 systems to test connectivity from Hb-IPN onto gsc2 and rln3 neurons.

The experiments are convincing but the choice of the duration of the stimulation (5s) is not adequate to test for direct connectivity: the authors should make sure that response in gsc2 neurons is observed with short duration (50ms-1s max).

As noted above:

“As the activity of the gsc2 neurons is already increased by 1.8 fold (± 0.28) within the first frame that the laser is activated (duration ~200 msec), it is unlikely that that the observed response is due to non-specific activation induced by the long light pulse.”

note: Specify that the gsc2 neurons tested are in NI.

We have edited the text accordingly in the Results section titled Afferent input to the NI from the dHb-IPN pathway.

b) for the response to shock: in the example shown for rln3 neurons, the activity differs before and after the shock with long phases of inhibition that were not seen before. Is it representative? the authors should carefully stare at their data & make sure there is no difference in activity patterns after shock versus before.

We reexamined the responses for each of the rln3a neurons individually and confirmed that, although oscillations in activity are frequent, the apparent inhibition (excursions below baseline) are an idiosyncratic feature of the particular example shown.

(3) motor activity assay:

a) there seems to be a misconception in the use of the word "bout" to estimate in panels H and I bout distance and duration and the analysis should be performed with the criterion used by all in the motor field:

As we know now well based on the work of many labs on larval zebrafish (Orger, Baier, Engert, Wyart, Burgess, Portugues, Bianco, Scott, ...), a bout is defined as a discrete locomotor event corresponding to a distance swam of typically 1-6mm, bout duration is typically 200ms and larvae exhibit a bout every s or so during exploration (see Mirat et al Frontiers 2013; Marques et al Current Biology 2018; Rajan et al. Cell Reports 2022).

Since the larval zebrafish has a low Reynolds number, it does not show much glide and its movement corresponds widely to the active phase of the tail beats.

Instead of detecting the active (moving) frames as bouts, the authors however estimate these values quite off that indicate an error of calibration in the detection of a movement: a bout cannot last for 5-10s, nor can the fish swim for more than 1 cm per bout (in the definition of the authors, bout last for 5-10 s, and bout correspond to 10 cm as 50 cm is covered in 5 bouts).

The authors should therefore distinguish the active (moving) from inactive (immobile) phase of the behavior to define bouts & analyze the corresponding distance travelled and duration of active swimming. They would also benefit from calculating the % of time spent swimming in order to test whether the fish with ablated rln3 neurons change the fraction of the time spent swimming.

As noted above:

Our recordings capture the entire arena that the larva can explore in the experiment and therefore lack the spatial resolution to capture and analyze the tail beat. Rather, we measured the frequency and length of phases of movement in which the larva shows no more than 1 second of immobility. To avoid confusion with studies that measure bouts from the onset of tail movement, we removed this term from the manuscript and refer to activity as phases of movement.

Note that a duration in seconds is not a length and that the corresponding symbol for seconds in a scientific publication is "s" and not "sec".

We have corrected this.

b) controls in these experiments are key as many clutches differ in their spontaneous exploration and there is a lot of variation for 2 min long recordings (baseline is 115s). The authors specify that the control unablated are a mix of siblings; they should show us how the ablated transgenic animals compare to the non ablated transgenic animals of the same clutch.

The unablated Tg(gsc2:QF2)c721; Tg(QUAS:GFP)c578 and Tg(rln3a:QF2, he1.1:YFP)c836; Tg(QUAS:GFP)c578 larvae in the control group are siblings of ablated larvae. We repeated the analyses using either the Tg(gsc2:QF2)c721; Tg(QUAS:GFP)c578 or Tg(rln3a:QF2, he1.1:YFP)c836; Tg(QUAS:GFP)c578 larvae only as controls and added the results in Figure 8-3. Although the statistical power is slightly reduced due to a smaller number of samples in the control group, the conclusions are the same, as the behavior of Tg(gsc2:QF2)c721; Tg(QUAS:GFP)c578 and Tg(rln3a:QF2, he1.1:YFP)c836; Tg(QUAS:GFP)c578 unablated larvae is indistinguishable.

Minor comments:

(1) Anatomy :

• Add precision in the anatomy in Figure 1:

• Improve contrast for cckb.

The contrast is determined by the signal to background ratio from the fluorescence in situ hybridization. Increasing the brightness would increase both the signal and the background, as any modification must be applied to the whole image.

• since the number of neurons seems low in each category, could you quantify the number of rln3+, nmbb+, gsc2+, cckb+ neurons in NI?

Quantification of neuronal numbers has been added to the first Results section titled Identification of gsc2 neurons in the Nucleus Incertus, lines 219-224.

note: indicate duration for the integral of the DF/F in s and not in frames.

We have added this in the legends for Figures 6 and 7 and in Materials and Methods.

(2) Genetic tools:

To generate a driver line for the rln3+ neurons using the Q system, the authors used the promoter for the hatching gland in order to drive expression in a structure outside of the nervous system that turns on early and transiently during development: this is a very elegant approach that should be used by many more researchers.

If the her1 construct was integrate together with the QF2 in the first exon of the rln3 locus as shown in Figure 2, the construct should not be listed with a ";" instead of a "," behind rln3a:QF2 in the transgene name. Please edit the transgene name accordingly.

We have edited the text accordingly.

(3) Typos:

GABAergic neurons is misspelled twice in Figure 3.

Thank you for catching this. We have corrected the misspellings.

Reviewer #3 (Recommendations For The Authors):

• More analysis should be done to better characterize the calcium activity of gsc2 and rln3a populations. Specifically:

Spontaneous activity is estimated by finding peaks in the time-series data, but the example in Fig7 raises concerns about this process: Two peaks for the gsc2 cell are identified while numerous other peaks of apparently similar SNR are not detected. Moreover, the inset images suggest GCaMP7a expression might be weaker in the gsc2 transgenic and as such, differences in peak count might be related to the SNR of the recordings rather than underlying activity. Overall, the process for estimating spontaneous activity should be more rigorous.

To not solely rely on the identification of peaks in the calcium traces, we also plotted histograms of the amplitudes of the calcium signals for the rln3a and gsc2 neurons. The histograms show that the amplitudes of the rln3a calcium signals frequently occur at small and large values (suggesting large fluctuations in activity), whereas the amplitudes of the gsc2 calcium signals occur most frequently at median values. We added this analysis to a revised Figure 7.

Interestingly, there are a number of large negative excursions in the calcium data for the rln3a cell - what is the authors' interpretation of these? Could it be that presynaptic inhibition via GABA-B receptors in dIPN might influence dIPN-innervating rln3a neurons?

As noted above:

We reexamined the responses for each of the rln3a neurons individually and confirmed that, although oscillations in activity are frequent, the apparent inhibition (excursions below baseline) are an idiosyncratic feature of the particular example shown.

Regarding shock-evoked activity, the authors state "rln3a neurons showed ... little response to shock", yet the immediate response after shock appears very similar in gsc2 vs rln3a cells (approx 30 units on the dF/F scale). The subsequent time-course of the response is what appears to distinguish gsc2 versus rln3a; it might thus be useful to separately quantify the amplitude and decay time constant of the shock evoked response for the two populations.

The reviewer is correct that the difference between the gsc2 and rln3a neurons in the response to shock is dependent on the duration of time post-shock that is analyzed. Thus, the more relevant feature is the length of the response rather than the size. To reflect this, we compared the average length of responses for the gsc2 and rln3a neurons. We have now added this analysis to Figure 7 and updated the text accordingly.

• The difference in spontaneous locomotor behavior is interesting and the example tracking data suggests there might also be differences in turn angle distribution and/or turn chain length following rln3 NI ablations. I would recommend the authors consider exploring this.

Thank you for this suggestion. We wrote additional code to quantify turning behavior and found that larvae with rln3a NI neurons ablated do indeed have a statistically significant increase in turning compared to other groups. We now show this analysis as Figure 8-2 and we added an explanation of the quantification of turning behavior to the Methods section titled Locomotor assay.

• I didn't follow the reasoning in the discussion that activity of rln3a cells may control transitions between phases of behavioral activity and inactivity. The events (at least those that are detected) in Fig7 occur with an average interval exceeding 30 s, yet swim bouts occur at a frequency around 1 Hz. The authors should clarify their hypothesis about how these disparate timescales might be connected.

As noted above:

Our recordings capture the entire arena that the larva can explore in the experiment and therefore lack the spatial resolution to capture and analyze the tail beat. Rather, we measure the frequency and length of phases of movement in which the larva shows no more than 1 second of immobility. To avoid confusion with studies that measure bouts from the onset of tail movement, we removed this term from the manuscript and refer to activity as phases of movement.

• Fig2-2: Images are ordered from (A, B, C) anterior to (A', B', C') posterior. Its not clear what this means and images appear to be in sequence A, A', B, B'.... please clarify and consider including a cartoon of the brain in sagittal view showing location of sections indicated.

We clarified the text in the Figure 2-2 legend and added a drawing of the brain showing the location of the sections.

• In Fig7, why are 300 frames analyzed pre/post shock? Even for gsc2, the response appears complete in ~100 frames.

Reviewer #2 also pointed out that the difference between the gsc2 and rln3a neurons in the response to shock is dependent on the duration of time post-shock that is analyzed. Thus, the more relevant feature is the length of the response rather than the size. To reflect this, we compared the average length of response for the gsc2 and rln3a neurons and modified the text and Figure as described above.

• What are the large negative excursions in the calcium signal in the rln3a data (Fig7E)?

See response to Reviewer # 2, repeated below:

We looked through each of the responses of individual rln3a neuron and confirmed that, although oscillations in activity are frequent among the rln3a neurons, the apparent inhibition (excursions below baseline) are an idiosyncratic feature of the particular example shown.

• There are several large and apparently perfectly straight lines in the fish tracking examples (Fig8) suggestive of tracking errors (ie. where the tracked centroid instantaneously jumps across the camera frame). Please investigate these and include analysis of the distribution of swim velocities to support the validity of the tracking data.

The reason for this is indeed imperfect tracking resulting in frames in which the tracker does not detect the larva. The result is that the larva appears to move 1 cm or more in a single frame. However, analysis of the distribution of distances across all frames shows that these events (movement of 1 cm or more in a single frame) are rare (less than 0.04%), and there are no systematic differences that would explain the differences in locomotor behavior presented in Fig. 8. A summary of the data is as follows:

Controls: 0.0249% of distances 1 cm or greater gsc2 neurons ablated: 0.0302% of distances 1 cm or greater rln3a NI neurons ablated: 0.0287% of distances 1 cm or greater rln3a PAG neurons ablated: 0.0241% of distance 1 cm or greater

• Insufficient detail is provided in the methods about how swim bouts are detected (and their durations extracted) from the centroids tracking data. Please expand detail in this section.

We added an explanation to the Methods section titled Locomotor assay.

Author response:

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

eLife assessment:

This study uses carefully designed experiments to generate a useful behavioural and neuroimaging dataset on visual cognition. The results provide solid evidence for the involvement of higher-order visual cortex in processing visual oddballs and asymmetry. However, the evidence provided for the very strong claims of homogeneity as a novel concept in vision science, separable from existing concepts such as target saliency, is inadequate.

We appreciate the positive and balanced assessment from the reviewers. We agree that visual homogeneity is similar to existing concepts such as target saliency. We have tried our best to articulate our rationale for defining it as a novel concept. However, the debate about whether visual homogeneity is novel or related to existing concepts is completely beside the point, since that is not the key contribution of our study.

Our key contribution is our quantitative model for how the brain could be solving generic visual tasks by operating on a feature space. In the literature there are no theories regarding the decision-making process by which the brain could be solving generic visual tasks. In fact, oddball search tasks, same-different tasks and symmetry tasks are never even mentioned in the same study because it is tacitly assumed that the underlying processes are completely different! Our work brings together these disparate tasks by proposing a specific computation that enables the brain to solve both types of tasks and providing evidence for it. This specific computation is a well-defined, falsifiable model that will need to be replicated, elaborated and refined by future studies.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors define a new metric for visual displays, derived from psychophysical response times, called visual homogeneity (VH). They attempt to show that VH is explanatory of response times across multiple visual tasks. They use fMRI to find visual cortex regions with VH-correlated activity. On this basis, they declare a new visual region in the human brain, area VH, whose purpose is to represent VH for the purpose of visual search and symmetry tasks.

Thank you for your concise summary. We appreciate your careful reading and thoughtful and constructive comments.

Strengths:

The authors present carefully designed experiments, combining multiple types of visual judgments and multiple types of visual stimuli with concurrent fMRI measurements. This is a rich dataset with many possibilities for analysis and interpretation.

Thank you for your accurate assessment of the strengths of our study.

Weaknesses:

The datasets presented here should provide a rich basis for analysis. However, in this version of the manuscript, I believe that there are major problems with the logic underlying the authors' new theory of visual homogeneity (VH), with the specific methods they used to calculate VH, and with their interpretation of psychophysical results using these methods. These problems with the coherency of VH as a theoretical construct and metric value make it hard to interpret the fMRI results based on searchlight analysis of neural activity correlated with VH.

We appreciate your concerns, and have tried our best to respond to them fully against your specific concerns below.

In addition, the large regions of VH correlations identified in Experiments 1 and 2 vs. Experiments 3 and 4 are barely overlapping. This undermines the claim that VH is a universal quantity, represented in a newly discovered area of the visual cortex, that underlies a wide variety of visual tasks and functions.

We agree with you that the VH regions defined using symmetry task and search task do not overlap completely (as we have shown in Figure S13). However this is to be expected for several reasons. First, the images in the symmetry task were presented at fixation, whereas the images in the visual search task were presented peripherally. Second, the lack of overlap could be due to variations across individuals. Indeed, considerable individual variability has been observed in the location of category-selective regions such as VWFA (Glezer and Riesenhuber 2013) and FFA (Weiner and Grill-Spector, 2012). We propose that testing the same participants on both search and symmetry tasks would reveal overlapping VH regions. We now acknowledge these issues in the Results (p. 26).

Maybe I have missed something, or there is some flaw in my logic. But, absent that, I think the authors should radically reconsider their theory, analyses, and interpretations, in light of the detailed comments below, to make the best use of their extensive and valuable datasets combining behavior and fMRI. I think doing so could lead to a much more coherent and convincing paper, albeit possibly supporting less novel conclusions.

We appreciate your concerns. We have tried our best to respond to them fully against your specific concerns below.

THEORY AND ANALYSIS OF VH

(1) VH is an unnecessary, complex proxy for response time and target-distractor similarity. VH is defined as a novel visual quality, calculable for both arrays of objects (as studied in Experiments 1-3) and individual objects (as studied in Experiment 4). It is derived from a center-to-distance calculation in a perceptual space. That space in turn is derived from the multi-dimensional scaling of response times for target-distractor pairs in an oddball detection task (Experiments 1 and 2) or in a same-different task (Experiments 3 and 4).

The above statements are not entirely correct. Experiments 1 & 3 are oddball visual search experiments. Their purpose was to estimate the underlying perceptual space of objects.

Proximity of objects in the space is inversely proportional to response times for arrays in which they were paired. These response times are higher for more similar objects. Hence, proximity is proportional to similarity. This is visible in Fig. 2B as the close clustering of complex, confusable animal shapes.

VH, i.e. distance-to-center, for target-present arrays, is calculated as shown in Fig. 1C, based on a point on the line connecting the target and distractors. The authors justify this idea with previous findings that responses to multiple stimuli are an average of responses to the constituent individual stimuli. The distance of the connecting line to the center is inversely proportional to the distance between the two stimuli in the pair, as shown in Fig. 2D. As a result, VH is inversely proportional to the distance between the stimuli and thus to stimulus similarity and response times. But this just makes VH a highly derived, unnecessarily complex proxy for target-distractor similarity and response time. The original response times on which the perceptual space is based are far more simple and direct measures of similarity for predicting response times.

We agree that VH brings no explanatory power to target-present searches, since target-present response times are a direct estimate of target-distractor similarity. However, we are additionally explaining target-absent response times. Target-absent response times are well known to vary systematically with image properties, but why they do so have not been clear in the literature.

Our key conceptual advance lies in relating the neural response to a search array to the neural response of the constituent elements, and in proposing a decision variable using which participants can make both target-present and target-absent judgements on any search array.

(2) The use of VH derived from Experiment 1 to predict response times in Experiment 2 is circular and does not validate the VH theory.

The use of VH, a response time proxy, to predict response times in other, similar tasks, using the same stimuli, is circular. In effect, response times are being used to predict response times across two similar experiments using the same stimuli. Experiment 1 and the target present condition of Experiment 2 involve the same essential task of oddball detection. The results of Experiment 1 are converted into VH values as described above, and these are used to predict response times in Experiment 2 (Fig. 2F). Since VH is a derived proxy for response values in Experiment 1, this prediction is circular, and the observed correlation shows only consistency between two oddball detection tasks in two experiments using the same stimuli.

We agree that it would be circular to use oddball search times in Experiment 1 to explain only target-present search times in Experiment 2, since they basically involve the same searches. However, we are explaining both target-present and target-absent search times in a unified framework; systematic variations in target-absent search times have been noted in the literature but never really explained. One could still simply say that target-absent search times are some function of the target-present search times, but this still doesn’t provide an explanation for how participants are making target-present and absent decisions. The existing literature contains models for how visual search might occur for a specific target and distractor but does not elucidate how participants might perform generic visual search where target and distractors are not known in advance.

Our key conceptual advance lies in relating the neural response to a search array to the neural response of the constituent elements, and in proposing a decision variable using which participants can make both target-present and target-absent judgements on any search array.

(3) The negative correlation of target-absent response times with VH as it is defined for target-absent arrays, based on the distance of a single stimulus from the center, is uninterpretable without understanding the effects of center-fitting. Most likely, center-fitting and the different VH metrics for target-absent trials produce an inverse correlation of VH with target-distractor similarity.

We see no cause for concern with the center-fitting procedure, for several reasons. First, the best-fitting center remained stable despite many randomly initialized starting points. Second, the best-fitting center derived from one set of objects was able to predict the target-absent and target-present responses of another set of objects. Finally, the VH obtained for each object (i.e. distance from the best-fitting center) is strongly correlated with the average distance of that object from all other objects (Figure S1A). We have now clarified this in the Results (p. 11).

The construction of the VH perceptual space also involves fitting a "center" point such that distances to center predict response times as closely as possible. The effect of this fitting process on distance-to-center values for individual objects or clusters of objects is unknowable from what is presented here. These effects would depend on the residual errors after fitting response times with the connecting line distances. The center point location and its effects on the distance-to-center of single objects and object clusters are not discussed or reported here.

While it is true that the optimal center needs to be found by fitting to the data, there no particular mystery to the algorithm: we are simply performing a standard gradient-descent to maximize the fit to the data. We have described the algorithm clearly and are making our codes public. We find the algorithm to yield stable optimal centers despite many randomly initialized starting points. We find the optimal center to be able to predict responses to entirely novel images that were excluded during model training. We are making no assumption about the location of centre with respect to individual points. Therefore, we see no cause for concern regarding the center-finding algorithm.

Yet, this uninterpretable distance-to-center of single objects is chosen as the metric for VH of target-absent displays (VHabsent). This is justified by the idea that arrays of a single stimulus will produce an average response equal to one stimulus of the same kind. However, it is not logically clear why response strength to a stimulus should be a metric for homogeneity of arrays constructed from that stimulus, or even what homogeneity could mean for a single stimulus from this set. It is not clear how this VHabsent metric based on single stimuli can be equated to the connecting line VH metric for stimulus pairs, i.e. VHpresent, or how both could be plotted on a single continuum.

Most visual tasks, such as finding an animal, are thought to involve building a decision boundary on some underlying neural representation. Even visual search has been portrayed as a signal-detection problem where a particular target is to be discriminated from a distractor. However none of these formulations work in the case of generic visual tasks, where the target and distractor identities are unknown. We are proposing that, when we view a search array, the neural response to the search array can be deduced from the neural responses to the individual elements using well known rules, and that decisions about an oddball target being present or absent can be made by computing the distance of this neural response from some canonical mean firing rate of a population of neurons. This distance to center computation is what we denote as visual homogeneity. We have revised our manuscript throughout to make this clearer and we hope that this helps you understand the logic better.

It is clear, however, what should be correlated with difficulty and response time in the target-absent trials, and that is the complexity of the stimuli and the numerosity of similar distractors in the overall stimulus set. The complexity of the target, similarity with potential distractors, and the number of such similar distractors all make ruling out distractor presence more difficult. The correlation seen in Fig. 2G must reflect these kinds of effects, with higher response times for complex animal shapes with lots of similar distractors and lower response times for simpler round shapes with fewer similar distractors.

You are absolutely correct that the stimulus complexity should matter, but there are no good measures for stimulus complexity. But considering what factors are correlated with target-absent response times is entirely different from asking what decision variable or template is being used by participants to solve the task.

The example points in Fig. 2G seem to bear this out, with higher response times for the deer stimulus (complex, many close distractors in the Fig. 2B perceptual space) and lower response times for the coffee cup (simple, few close distractors in the perceptual space). While the meaning of the VH scale in Fig. 2G, and its relationship to the scale in Fig. 2F, are unknown, it seems like the Fig. 2G scale has an inverse relationship to stimulus complexity, in contrast to the expected positive relationship for Fig. 2F. This is presumably what creates the observed negative correlation in Fig. 2G.

Taken together, points 1-3 suggest that VHpresent and VHabsent are complex, unnecessary, and disconnected metrics for understanding target detection response times. The standard, simple explanation should stand. Task difficulty and response time in target detection tasks, in both present and absent trials, are positively correlated with target-distractor similarity.

Respectfully, we disagree with your assessment. Your last point is not logically consistent though: response times for target-absent trials cannot be correlated with any target-distractor similarity since there is no target in the first place in a target-absent array. We have shown that target-absent response times are in fact, independent of experimental context, which means that they index an image property that is independent of any reference target (Results, p. 15; Section S4). This property is what we define as visual homogeneity.

I think my interpretations apply to Experiments 3 and 4 as well, although I find the analysis in Fig. 4 especially hard to understand. The VH space in this case is based on Experiment 3 oddball detection in a stimulus set that included both symmetric and asymmetric objects. However, the response times for a very different task in Experiment 4, a symmetric/asymmetric judgment, are plotted against the axes derived from Experiment 3 (Fig. 4F and 4G). It is not clear to me why a measure based on oddball detection that requires no use of symmetry information should be predictive of within-stimulus symmetry detection response times. If it is, that requires a theoretical explanation not provided here.

We are using an oddball detection task to estimate perceptual dissimilarity between objects, and construct the underlying perceptual representation of both symmetric and asymmetric objects. This enabled us to then ask if some distance-to-center computation can explain response times in a symmetry detection task, and obtain an answer in the affirmative. We have reworked the text to make this clear.

(4) Contrary to the VH theory, same/different tasks are unlikely to depend on a decision boundary in the middle of a similarity or homogeneity continuum.

We have provided empirical proof for our claims, by showing that target-present response times in a visual search task are correlated with “different” responses in the same-different task, and that target-absent response times in the visual search task are correlated with “same” responses in the same-different task (Section S3).

The authors interpret the inverse relationship of response times with VHpresent and VHabsent, described above, as evidence for their theory. They hypothesize, in Fig. 1G, that VHpresent and VHabsent occupy a single scale, with maximum VHpresent falling at the same point as minimum VHabsent. This is not borne out by their analysis, since the VHpresent and VHabsent value scales are mainly overlapping, not only in Experiments 1 and 2 but also in Experiments 3 and 4. The authors dismiss this problem by saying that their analyses are a first pass that will require future refinement. Instead, the failure to conform to this basic part of the theory should be a red flag calling for revision of the theory.

We respectfully disagree – by no means did we dismiss this problem! In fact, we have explicitly acknowledged this by saying that VH does not explain all the variance in the response times, but nonetheless explains substantial variance and might form the basis for an initial guess or a fast response. The remaining variance might be explained by processes that involve more direct scrutiny. Please see Results, page 10 & 22.

The reason for this single scale is that the authors think of target detection as a boundary decision task, along a single scale, with a decision boundary somewhere in the middle, separating present and absent. This model makes sense for decision dimensions or spaces where there are two categories (right/left motion; cats vs. dogs), separated by an inherent boundary (equal left/right motion; training-defined cat/dog boundary). In these cases, there is less information near the boundary, leading to reduced speed/accuracy and producing a pattern like that shown in Fig. 1G.

The key conceptual advance of our study is that we show that even target/present, same/different or symmetry judgements can be fit into the standard decision-making framework.

This logic does not hold for target detection tasks. There is no inherent middle point boundary between target present and target absent. Instead, in both types of trials, maximum information is present when the target and distractors are most dissimilar, and minimum information is present when the target and distractors are most similar. The point of greatest similarity occurs at the limit of any metric for similarity. Correspondingly, there is no middle point dip in information that would produce greater difficulty and higher response times. Instead, task difficulty and response times increase monotonically with the similarity between targets and distractors, for both target present and target absent decisions. Thus, in Figs. 2F and 2G, response times appear to be highest for animals, which share the largest numbers of closely similar distractors.

Unfortunately, your logic does not boil down to any quantitative account, since you are using vague terms like “maximum information”. Further, any argument based solely on item similarity to explain visual search or symmetry responses cannot explain systematic variations observed for target-absent arrays and for symmetric objects, for the reasons below.

If target-distractor dissimilarity were the sole driver of response times, target-absent judgements should always take the longest time since the target and distractor have zero similarity, with no variation from one image to another. This account does not explain why target-absent response times vary so systematically.

Similarly, if symmetry judgements are solely based on comparing the dissimilarity between two halves of an object, there should be no variation in the response times of symmetric objects since the dissimilarity between their two halves is zero. However we do see systematic variation in the response times to symmetric objects.

DEFINITION OF AREA VH USING fMRI

(1) The area VH boundaries from different experiments are nearly completely non-overlapping.

In line with their theory that VH is a single continuum with a decision boundary somewhere in the middle, the authors use fMRI searchlight to find an area whose responses positively correlate with homogeneity, as calculated across all of their target present and target absent arrays. They report VH-correlated activity in regions anterior to LO. However, the VH defined by symmetry Experiments 3 and 4 (VHsymmetry) is substantially anterior to LO, while the VH defined by target detection Experiments 1 and 2 (VHdetection) is almost immediately adjacent to LO. Fig. S13 shows that VHsymmetry and VHdetection are nearly non-overlapping. This is a fundamental problem with the claim of discovering a new area that represents a new quantity that explains response times across multiple visual tasks. In addition, it is hard to understand why VHsymmetry does not show up in a straightforward subtraction between symmetric and asymmetric objects, which should show a clear difference in homogeneity. • Actually VHsymmetry is apparent even in a simple subtraction between symmetric and asymmetric objects (Figure S10). The VH regions identified using the visual search task and symmetry task have a partial overlap, not zero overlap as you are incorrectly claiming.

We have noted that it is not straightforward to interpret the overlap, since there are many confounding factors. One reason could simply be that the stimuli in the symmetry task were presented at fixation, whereas the visual search arrays contained items exclusively in the periphery. Another that the participants in the two tasks were completely different, and the lack of overlap is simply due to inter-individual variability. Testing the same participants in two tasks using similar stimuli would be ideal but this is outside the scope of this study. We have acknowledged these issues in the Results (p. 26) and in the Supplementary Material (Section S8).

(2) It is hard to understand how neural responses can be correlated with both VHpresent and VHabsent.

The main paper results for VHdetection are based on both target-present and target-absent trials, considered together. It is hard to interpret the observed correlations, since the VHpresent and VHabsent metrics are calculated in such different ways and have opposite correlations with target similarity, task difficulty, and response times (see above). It may be that one or the other dominates the observed correlations. It would be clarifying to analyze correlations for target-present and target-absent trials separately, to see if they are both positive and correlated with each other.

Thanks. The positive correlation between VH and neural response holds even when we do the analysis separately for target-present and -absent searches (correlation between neural response in VH region and visual homogeneity (n = 32, r = 0.66, p < 0.0005 for target-present searches & n = 32, r = 0.56, p < 0.005 for target-absent searches).

(3) The definition of the boundaries and purpose of a new visual area in the brain requires circumspection, abundant and convergent evidence, and careful controls.

Even if the VH metric, as defined and calculated by the authors here, is a meaningful quantity, it is a bold claim that a large cortical area just anterior to LO is devoted to calculating this metric as its major task. Vision involves much more than target detection and symmetry detection. The cortex anterior to LO is bound to perform a much wider range of visual functionalities. If the reported correlations can be clarified and supported, it would be more circumspect to treat them as one byproduct of unknown visual processing in the cortex anterior to LO, rather than treating them as the defining purpose for a large area of the visual cortex.

We totally agree with you that reporting a new brain region would require careful interpretation and abundant and converging evidence. However, this requires many studies worth of work, and historically category-selective regions like the FFA have achieved consensus only after they were replicated and confirmed across many studies. We believe our proposal for the computation of a quantity like visual homogeneity is conceptually novel, and our study represents a first step that provides some converging evidence (through replicable results across different experiments) for such a region. We have reworked our manuscript to make this point clearer (Discussion, p 32).

Reviewer #2 (Public Review):

Summary:

This study proposes visual homogeneity as a novel visual property that enables observers perform to several seemingly disparate visual tasks, such as finding an odd item, deciding if two items are the same, or judging if an object is symmetric. In Experiment 1, the reaction times on several objects were measured in human subjects. In Experiment 2, the visual homogeneity of each object was calculated based on the reaction time data. The visual homogeneity scores predicted reaction times. This value was also correlated with the BOLD signals in a specific region anterior to LO. Similar methods were used to analyze reaction time and fMRI data in a symmetry detection task. It is concluded that visual homogeneity is an important feature that enables observers to solve these two tasks.

Strengths:

(1) The writing is very clear. The presentation of the study is informative.

(2) This study includes several behavioral and fMRI experiments. I appreciate the scientific rigor of the authors.

We are grateful to you for your balanced assessment and constructive comments.

Weaknesses:

(1) My main concern with this paper is the way visual homogeneity is computed. On page 10, lines 188-192, it says: "we then asked if there is any point in this multidimensional representation such that distances from this point to the target-present and target-absent response vectors can accurately predict the target-present and target-absent response times with a positive and negative correlation respectively (see Methods)". This is also true for the symmetry detection task. If I understand correctly, the reference point in this perceptual space was found by deliberating satisfying the negative and positive correlations in response times. And then on page 10, lines 200-205, it shows that the positive and negative correlations actually exist. This logic is confusing. The positive and negative correlations emerge only because this method is optimized to do so. It seems more reasonable to identify the reference point of this perceptual space independently, without using the reaction time data. Otherwise, the inference process sounds circular. A simple way is to just use the mean point of all objects in Exp 1, without any optimization towards reaction time data.

We disagree with you since the same logic applies to any curve-fitting procedure. When we fit data to a straight line, we are finding the slope and intercept that minimizes the error between the data and the straight line, but we would hardly consider the process circular when a good fit is achieved – in fact we take it as a confirmation that the data can be fit linearly. In the same vein, we would not have observed a good fit to the data, if there did not exist any good reference point relative to which the distances of the target-present and target-absent search arrays predicted these response times.

In Section S1, we have already reported that the visual homogeneity estimates for each object is strongly correlated with the average distance of each object to all other objects (r = 0.84, p<0.0005, Figure S1). Second, to confirm that the results we obtained are not due to overfitting, we have already reported a cross-validation analysis, where we removed all searches involving a particular image and predicted these response times using visual homogeneity. This too revealed a significant model correlation confirming that our results are not due to overfitting.

(2) On page 11, lines 214-221. It says: "these findings are non-trivial for several reasons". However, the first reason is confusing. It is unclear to me why "it suggests that there are highly specific computations that can be performed on perceptual space to solve oddball tasks". In fact, these two sentences provide no specific explanation for the results.

We have now revised the text to make it clearer (Results, p. 11).

(3) The second reason is interesting. Reaction times in target-present trials can be easily explained by target-distractor similarity. But why does reaction time vary substantially across target-absent stimuli? One possible explanation is that the objects that are distant from the feature distribution elicit shorter reaction times. Here, all objects constitute a statistical distribution in the feature (perceptual) space. There is certainly a mean of this distribution. Some objects look like outliers and these outliers elicit shorter reaction times in the target-absent trials because outlier detection is very salient.

One might argue that the above account is merely a rephrasing of the idea of visual homogeneity proposed in this study. If so, feature saliency is not a new account. In other words, the idea of visual homogeneity is another way of reiterating the old feature saliency theory.

Thank you for this interesting point. We don’t necessarily see a contradiction. However, we are proposing a quantitative decision variable that the brain could be using to make target present/absent judgements.

(4) One way to reject the feature saliency theory is to compare the reaction times of the objects that are very different from other objects (i.e., no surrounding objects in the perceptual space, e.g., the wheel in the lower right corner of Fig. 2B) with the objects that are surrounded by several similar objects (e.g., the horse in the upper part of Fig. 2B). Also, please choose the two objects with similar distance from the reference point. I predict that the latter will elicit longer reaction times because they can be easily confounded by surrounding similar objects (i.e., four-legged horses can be easily confounded by four-legged dogs). If the density of object distribution per se influences the visual homogeneity score, I would say that the "visual homogeneity" is essentially another way of describing the distributional density of the perceptual space.

We agree with you, and we have indeed found that visual homogeneity estimates from our model are highly correlated with the average distance of an object relative to all other objects. However, we performed several additional experiments to elucidate the nature of target-absent response times. We find that they are unaffected by whether these searches are performed in the midst of similar or dissimilar objects (Section S4, Experiment S6), and even when the same searches are performed among nearby sets of objects with completely uncorrelated average distances (Section S4, Experiment S7). We have now reworked the text to make this clearer.

(5) The searchlight analysis looks strange to me. One can easily perform a parametric modulation by setting visual homogeneity as the trial-by-trial parametric modulator and reaction times as a covariate. This parametric modulation produces a brain map with the correlation of every voxel in the brain. On page 17 lines 340-343, it is unclear to me what the "mean activation" is.

We have done something similar. For each region we took the mean activation at each voxel as the average activation 3x3x3 voxel neighborhood in the brain, and took its correlation with visual homogeneity. We have now reworked this to make it clearer (Results, p. 16).

Minor points

(1) In the intro, it says: "using simple neural rules..." actually it is very confusing what "neural rules" are here. Better to change it to "computational principles" or "neural network models"??

We have now replaced this with “using well-known principles governing multiple object representations”.

(2) In the intro, it says: "while machine vision algorithms are extremely successful in solving feature-based tasks like object categorization (Serre, 2019), they struggle to solve these generic tasks (Kim et al., 2018; Ricci et al. 2021). These are not generic tasks. They are just a specific type of visual task-judging relationship between multiple objects. Moreover, a large number of studies in machine vision have shown that DNNs are capable of solving these tasks and even more difficult tasks. Two survey papers are listed here.

Wu, Q., Teney, D., Wang, P., Shen, C., Dick, A., & Van Den Hengel, A. (2017). Visual question answering: A survey of methods and datasets. Computer Vision and Image Understanding, 163, 21-40.

Małkiński, M., & Mańdziuk, J. (2022). Deep Learning Methods for Abstract Visual Reasoning: A Survey on Raven's Progressive Matrices. arXiv preprint arXiv:2201.12382.

Thank you for sharing these references. In fact, a recent study has shown that specific deep networks can indeed solve the same-different task (Tartaglini et al, 2023). However our broader point remains that the same-different or other such visual tasks are non-trivial for machine vision algorithms.

Reviewer #1 (Recommendations For The Authors):

Nothing to add to the public review. If my concerns turn out to be invalid, I apologize and will happily accept correction. If they are valid, I hope they will point toward a new version of this paper that optimizes the insights to be gained from this impressive dataset.

Reviewer #2 (Recommendations For The Authors):

My suggestions are as follows:

(1) Analyze the fMRI data using the parametric modulation approach first at the single-subject level and then perform group analysis.

To clarify, we have obtained image-level activations from each subject, and used it for all our analyses.

(2) Think about a way to redefine visual homogeneity from a purely image-computable approach. In other words, visual homogeneity should be first defined as an image feature that is independent of any empirical response data. And then use the visual homogeneity scores to predict reaction times.

While we understand what you mean, any image-computable representation such as from a deep network may carry its own biases and may not be an accurate representation of the underlying object representation. By contrast, neural dissimilarities in the visual cortex are strongly predictive of visual search oddball response times. That is why we used visual search oddball response times as a proxy for the underlying neural representation, and then asked whether some decision variable can be derived from this representation to explain both target present and absent judgements in visual search.

Author response:

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

eLife assessment

The authors provide convincing experimental evidence of extended motivational signals encoded in the mouse anterior cingulate cortex (ACC) that are implemented by the orbitofrontal cortex (OFC)-to-ACC signaling during learning. The results are valuable to the field of motivation and cognition. The experimental methods used were state-of-the-art. The manuscript would further benefit from theory-driven analyses to inform a mechanistic understanding, particularly for the single-cell calcium imaging results. These results will be of interest to those interested in cortical function, learning, and/or motivation.

We thank the reviewers for their thoughtful reading of our paper and providing constructive feedback. We have made the relevant changes to the manuscript to improve the writing and figures. We provide responses below to each of the reviewer’s comments.

Reviewer #1 (Public Review):

(1) An important conclusion (Figure 4) is that when mice are trained to run through no reward (N) cues in order to reach reward (R) cues, the OFC neurons projecting to ACC each respond to different specific events in a manner that ensures that collectively they tile the extended behavioural sequence. What I was less sure of was whether the ACC neurons do the same or not. Figure 3 suggests that on average ACC neurons maintain activity across N cues in order to get to R cues but I was not sure whether this was because all individual neurons did this or whether some had activity patterns like the OFC neurons projecting to ACC.

We agree that it remains uncertain what individual ACC neurons do during the extended behavioral sequence. We now include a few sentences in the discussion about what we hypothesize, as we did not perform the cellular resolution imaging to determine this:

“While we did not perform single-cell imaging of ACC in our task, we hypothesize that individual ACC neurons could encode the distribution of actions/opportunities47 (i.e. stop, run, lick, suppress lick) taken during R or N cues. ACC neurons could compute the relative value of the action taken such that more ACC neurons become recruited once mice learn to run out of N cues. The sustained increase in bulk ACC activity across N cue trials (Figure 2) could come from a stable sequence of individual neurons that encode the timescale of the actions taken. In this way, OFC projections would encode current motivation across N cues before learning, which then triggers ACC to compute the valuebased actions. Motivational signals in OFC would thus represent state since past rewards/goals, while in ACC these signals represent actions taken to pursue rewards/goals in the future.”

(2) Figure 1 versus Figure 2: There does not seem to be a particular motivation for whether chemogenetic inactivation or optogenetic inhibition were used in different experiments. I think that this is not problematic but, if I am wrong and there were specific reasons for performing each experiment in a certain way, then further clarification as to why these decisions were made would be useful. If there is no particular reason, then simply explaining that this is the case might stop readers from seeking explanations.

Thank you for this comment and we agree that clarification on this is important. We performed chemogenetic inhibition of ACC in Figure 1 to take a broad survey of behavioral effects throughout a 40-min long behavioral session, and performed optogenetic inhibition in Figure 2 because we wanted to restrict our inhibition to the few seconds of cue presentation during a behavioral session and across days. Furthermore, we wanted to combat any potential off-target effects that would come from repeated administration of CNO over the several days of training (Manvich et al 2018). We have included a couple sentences on page 4 to clarify this:

“We proceeded to test whether these motivation related signals in ACC are required for learning. To restrict our inhibition to cue presentation portions of our task, and combat any potential off-target effects of CNO31 from repeated administration across several days of training, we used optogenetic inhibition.”

(3) P5, paragraph 2. The authors argue that OFC and anteriomedial (AM) thalamic inputs into ACC are especially important for mediating motivation through N cues in order to reach R cues. Is this based on a statistical comparison between the activity in OFC or AM inputs as opposed to the other inputs?

We determined that OFC and AM thalamic inputs to ACC are particularly important by comparing the pre-cue activity in a reward-no reward-reward trial sequence (RNR; Figure 3B). Specifically, we performed paired t-tests comparing pre-cue activity between N and R cues, and found a statistically significant increase for R cues but only for the OFC and AM inputs, not for the BLA or LC inputs.

(4) P3, paragraph 2. Some papers by Khalighinejad and colleagues (eg Neuron 2020, Current Biology, 2022) might be helpful here in as much as they assess ACC roles in determining action frequency, initiation, and speed and mediating the relationship between reward availability and action frequency and speed.

We thank the reviewer for bringing these relevant papers to our attention. We have included these papers in our citations in this paragraph.

(5) Paragraph 1 "This learning is of a more deliberate, informed nature than habitual learning, as they are sensitive to the current value of outcomes and can lead to a novel sequence of actions for a desired outcome1-3." Should "they" be "it"?

This is correct, we have edited this in the manuscript.

Reviewer #2 (Public Review):

Impact:

The findings will be valuable for further research on the impact of motivational states on behaviour and cognition. The authors provided a promising concept of how persistent motivational states could be maintained, as well as established a novel, reproducible task assay. While experimental methods used are currently state-of-the-art, theoretical analysis seems to be incomplete/not extensive. We thank the reviewer for these comments. In our paper, we performed single-cell calcium imaging of OFC projection neurons to ACC to build a mechanistic understanding for the bulk ramp-like response we identified in these neurons with photometry. We identified ensembles of neurons that tile sequences of trials that match the bulk response, in particular a subset of neurons that are active at the time a reward (R) cue is reached after 2 no-reward (N) cues. We included a paragraph in the discussion to address future theory-driven analyses to address how computation is achieved by OFC projection neurons:

“We linked the ramp-like increase in neural activity in OFC to motivation, but several questions still remain about how motivation is computed and why it would be represented as a ramp. Motivation could be computed as a combination of several variables such as time since last reward, value of reward, and effort to reach future rewards. Future theorydriven analyses could determine how motivation is computed, and whether individual variables of time, value, and effort, are encoded as clusters of similar tuned neurons, or mixed and collectively represented at the population level. In either case, it is likely that a combined map of task space and value-information carried by OFC are being used to inform downstream regions, such as ACC, for adjusting behavior. ”

Reviewer #2 (Recommendations for the Authors):

Overall, the layout of the figures seems a little bit chaotic and makes it hard to understand the boundaries between panels.

We agree that the figure layout could be improved upon to aid the reader in moving from panel to panel. We have edited two of the main figures with layouts that are most irregular (Figures 2 and 4) to help with this.

Figures/text should include the promoters used for protein expression so that readers understand which cell types would be affected.

We have made sure to edit the figures to include the promoter of the viruses we used, and edited the text to include both the AAV serotype and promoter.

Discuss why it is necessary for multiple prefrontal areas to be involved in maintaining motivational signals.

We thank the reviewer for this comment. We believe that prefrontal areas would be recruited as tasks to study motivational states become more complex and require animals to keep track of task structure and perform value-guided actions. We have included a couple sentences in the final paragraph of the discussion about this:

“Our work showed the recruitment of multiple frontal cortical areas in this process, which is to be expected as animals are required to build, maintain, and use representations of task structure and value to drive learned, motivated behaviors47. Future work can build upon the task we developed here to determine how the frontal cortex maintains motivational states across many more cue-outcome associations, and how these associations may dynamically change across time48”.

Additionally, we included a short discussion on how in motivational signals differ between OFC and ACC in our work. We suggest OFC encodes current motivation before and after learning, which then leads ACC to represent learned actions taken and thus have a longer timescale motivational response (see response to Reviewer 1).

Minor: Page 4, Line 1: "increase" instead of "increases".

This is correct, we have edited this in the manuscript.

Author response:

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

eLife assessment

This study provides important insights into the role of neurexins as regulators of synaptic strength and timing at the glycinergic synapse between neurons of the medial nucleus of the trapezoid body and the lateral superior olive, key components of the auditory brainstem circuit involved in computing sound source location from differences in the intensity of sounds arriving at the two ears. Through an elegant combination of genetic manipulation, fluorescence in-situ hybridization, ex vivo slice electrophysiology, pharmacology, and optogenetics, the authors provide convincing evidence to support their claims. While further work is needed to reveal the mechanistic basis by which neurexins influence glycinergic neurotransmission, this work will be of interest to both auditory and synaptic neuroscientists.

We appreciate the recognition of the significance of our study in shedding light on the role of neurexins in regulating synaptic strength and timing at the glycinergic synapse. Indeed, further investigations are warranted to delve deeper into the specific role of each different variant of neurexins in the future. We hope that our work will spark more interest and collaboration in unraveling the complexities of molecular codes of synaptic function.

Public Reviews:

Reviewer #1 (Public Review):

Jiang et al. demonstrated that ablating Neurexins results in alterations to glycinergic transmission and its calcium sensitivity, utilizing a robust experimental system. Specifically, the authors employed rAAV-Cre-EGFP injection around the MNTB in Nrxn1/2/3 triple conditional mice at P0, measuring Glycine receptor-dependent IPSCs from postsynaptic LSO neurons at P13-14. Notably, the authors presented a clear reduction of 60% and 30% in the amplitudes of opto- and electric stimulation-evoked IPSCs, respectively. Additionally, they observed changes in kinetics, alterations in PPR, and sensitivity to lower calcium and the calcium chelator, EGTA, indicating solid evidence for changes in presynaptic properties of glycinergic transmission.

Furthermore, the authors uncovered an unexpected increase in sIPSC frequency without altering amplitude. Despite the reduction in evoked IPSC, immunostaining revealed an increase in GlyT2 and VGAT in TKO mice, supporting the notion of an increase in synapse number. However, the reviewer expresses caution regarding the authors' conclusion that "glycinergic neurotransmission likely by promoting the synapse formation/maintenance, which is distinct from the phenotypes observed in glutamatergic and GABAergic neurons (Chen et al., 2017; Luo et al., 2021)", as outlined in lines 173-175. The reviewer suggests that this statement may be overstated, pointing out the authors' own discussion in lines 254-265, which acknowledges multiple possibilities, including the potential that the increase in synapses is a consequence rather than a causal effect of Nrxn deletion.

We appreciate the reviewer’s thoughtful evaluation of our study. We agree that our conclusion regarding the promotion of synapse formation/maintenance may have been overstated and recognize the need for a more nuanced interpretation of our findings. Accordingly, we have revised our interpretation by discussing carefully the various possibilities that may cause the observed increase in synapse number in line 256-266.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Jiang et al., explore the role of neurexins at glycinergic MNTB-LSO synapses. The authors utilize elegant and compelling ex vivo slice electrophysiology to assess how the genetic conditional deletion of Nrxns1-3 impacts inhibitory glycinergic synaptic transmission and found that TKO of neurexins reduced electrically and optically evoked IPSC amplitudes, slowed optically evoked IPSC kinetics and reduced presynaptic release probability. The authors use classic approaches including reduced [Ca2+] in ACSF and EGTA chelation to propose that changes in these evoked properties are likely driven by the loss of calcium channel coupling. Intriguingly, while evoked transmission was impaired, the authors reported that spontaneous IPSC frequency was increased, potentially due to an increased number of synapses in LSO. Overall, this manuscript provides important insight into the role of neurexins at the glycinergic MNTP-LSO synapse and further emphasizes the need for continued study of both the non-redundant and redundant roles of neurexins.

We thank the reviewer for the strong comments and support of our work.

Strengths:

This well-written manuscript seamlessly incorporates mouse genetics and elegant ex vivo electrophysiology to identify a role for neurexins in glycinergic transmission at MNTB-LSO synapses. Triple KO of all neurexins reduced the amplitude and timing of evoked glycinergic synaptic transmission. Further, spontaneous IPSC frequency was increased. The evoked synaptic phenotype is likely a result of reduced presynaptic calcium coupling while the spontaneous synaptic phenotype is likely due to increased synapse numbers. While neuroligin-4 has been identified at glycinergic synapses, this study, to the best of my knowledge, is the first to study Nrxn function at these synapses.<br />

We again appreciate the positive feedback on the strengths of our study. We agree that the observed reduction in evoked synaptic transmission and the increase in spontaneous IPSC frequency provide intriguing insights into the function of neurexins in regulating glycinergic synaptic activity.

Weaknesses:

The data are compelling and report an intriguing functional phenotype. The role of Neurexins redundantly controls calcium channel coupling has been previously reported. Mechanistic insight would significantly strengthen this study.

We wholeheartedly agree with the reviewer that understanding how neurexins control calcium channel coupling at the presynaptic active zone is crucial for elucidating their role in synaptic transmission. While our current study has provided compelling evidence for the functional phenotypes of pan-neurexin deletion, we recognize the importance of investigating the underlying molecular mechanisms in future research. Exploring these mechanisms would undoubtedly enhance our understanding of neurexin function at various synapses and contribute to advancing the field.

The claim that triple KO of Nrxns from MNTB increases the number of synapses in LSO is not strongly supported.

We agree. Echoing the suggestion made by reviewer 1 (as mentioned above), we acknowledge that the claim regarding the increase in synapse numbers in the LSO following the triple knockout of neurexins from the MNTB was overstated. Consequently, we have revised our conclusions more carefully to reflect this adjustment.

Despite the stated caveats of measuring electrically evoked currents and the more robust synaptic phenotypes observed using optically evoked transmission, the authors rely heavily on electrical stimulation for most measurements.

We acknowledge that optogenetic stimulation offers crucial advantages, and we have provided a balanced discussion of the caveats associated with both methods in our manuscript. Additionally, we have conducted new optogenetic experiments specifically for measuring the paired-pulse ratio in control and Nrxn123 TKO mice. These results have been included as a new supplementary figure (Figure S2).

For experiments involving EGTA and low Ca2+ manipulations, we opted for electrical stimulation due to concerns regarding potential side effects of optogenetics, including the phototoxicity and photobleaching during prolonged light exposure.

The differential expression of individual neurexins might indicate that specific neurexins may dominantly regulate synaptic transmission, however, this possibility is not discussed in detail.

We thank the reviewer for bringing up this important point. The differential expression of individual neurexins indeed suggests that specific neurexins may play dominant roles in regulating synaptic transmission. While our study primarily focused on the collective impact of ablating all neurexins, we acknowledge the significance of exploring the specific contributions of individual neurexin isoforms in the future. Understanding the distinct roles of each neurexin isoform could provide valuable insights into the precise mechanisms underlying synaptic function and plasticity. We have added discussion in our revised manuscript Line223-230.

Reviewer #3 (Public Review):

Summary:

The authors investigate the hypothesis that neurexins serve a crucial role as regulators of the synaptic strength and timing at the glycinergic synapse between neurons of the medial nucleus of the trapezoid body (MNTB) and the lateral superior olivary complex (LSO). It is worth mentioning that LSO neurons are an integration station of the auditory brainstem circuit displaying high reliability and temporal precision. These features are necessary for computing interaural cues to derive sound source location from comparing the intensities of sounds arriving at the two ears. In this context, the authors' findings build up according to the hypothesis first by displaying that neurexins were expressed in the MNTB at varying levels. They followed this up with the deletion of all neurexins in the MNTB through the employment of a triple knock-out (TKO). Using electrophysiological recordings in acute brainstem slices of these TKO mice, they gathered solid evidence for the role of neurexins in synaptic transmission at this glycinergic synapse primarily by ensuring tight coupling of Ca2+ channels and vesicular release sites. Additionally, the authors uncovered a connection between the deletion of neurexins and a higher number of glycinergic synapses in TKO mice, for which they provided evidence in the form of immunostainings and related it to electrophysiological data on spontaneous release. Consequently, this investigation expands our knowledge on the molecular regulation of synaptic transmission at glycinergic synapses, as well as on the auditory processing at the level of the brainstem.

Strengths:

The authors demonstrate substantial results in support of the hypothesis of a critical role of neurexins for regulating glycinergic transmission in the LSO using various techniques. They provide evidence for the expression of neurexins in the MNTB and consecutively successfully generate and characterize the neurexin TKO. For their study on LSO IPSCs the authors transduced MNTB neurons by co-injection of virus-carrying Cre and ChR2 and subsequently optogenetically evoke release of glycine. As a result, they observed a significant reduction in amplitude and significantly slower rise and decay times of the IPSCs of the TKO in comparison with control mice in which MNTB neurons were only transduced with ChR2. Furthermore, they observed an increased paired pulse ratio (PPR) of LSO IPSCs in the TKO mice, indicating lower release probability. Elaborating on the hypothesis that neurexins are essential for the coupling of synaptic vesicles to Ca2+ channels, the authors show lowered Ca2+ sensitivity in the TKO mice. Additionally, they reveal convincing evidence for the connection between the increased frequency of spontaneous IPSC and the higher number of glycinergic synapses of the LSO in the TKO mice, revealed by immunolabeling against the glycinergic presynaptic markers GlyT2 or VGAT.

We thank the reviewer for the thoughtful and thorough evaluation of the significance of investigating the role of neurexins in glycinergic transmission at the MNTB-LSO synapse, particularly in the context of auditory processing and sound localization. The positive feedback is greatly appreciated.

Weaknesses:

The major concern is novelty as this work on the effects of pan-neurexin deletion in a glycinergic synapse is quite consistent with the authors' prior work on glutamatergic synapses (Luo et al., 2020). The authors might want to further work out novel aspects and strengthen the comparative perspective. Conceptually, the authors might want to be more clear about interpreting the results on the altered dependence of release on voltage-gated Ca2+ influx (Ca2+ sensitivity, coupling).

Regarding the reviewer’s concern about the novelty of our work, we acknowledge that our previous work has explored the effects of pan-neurexin deletion on glutamatergic synapses (Luo et al., 2020). However, we would like to point out that a novelty of our present study indeed stems from the exploration of how different types of synapses converge to employ the same mechanism of synaptic function, particularly in the context of neurexin-mediated regulation. Our previous study focused on glutamatergic synapses, the current study delves into the realm of glycinergic synapses, which represent a distinct population with unique properties and functions. Despite the differences between these synapse types, our findings reveal a commonality in the underlying mechanisms of synaptic regulation mediated by neurexins. This convergence of mechanisms across different synapse types highlights the fundamental role of neurexins in synaptic function and plasticity. By elucidating how neurexins regulate synaptic transmission at both excitatory and inhibitory synapses, we provide valuable insights into the general principles governing synaptic function. In addition, this comparative perspective may shed light on the complex interplay between excitatory and inhibitory neurotransmission, which is crucial for maintaining the balance of neuronal activity and network dynamics.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

During the developmental period spanning P3-P12, the MNTB-LSO synapses undergo a transition from GABAergic to glycinergic transmission. It is well-established that Neurexin plays a role in modulating GABAergic transmission. In the authors' experimental system, AAV was injected at P0, likely impacting GABAergic transmission, including potentially influencing synapse number, before subsequently affecting glycinergic transmission. A thoughtful discussion of how the experimental interventions might have influenced this developmental process and glycinergic transmission would enhance the clarity and interpretation of their findings.

We thank the reviewer for raising the interesting topic of the transmitter switch during neurodevelopment. Strong evidence using gerbils and rats as animal models demonstrates that the MNTB-LSO synapses undergo a shift from GABAergic to glycinergic during the early development. However, in a more recent study by Friauf and colleagues (Fisher et al., 2019), patch-clamp recordings in acute mouse brainstem slices at P4-P11 combined with pharmacological blockade of GABAA receptors and/or glycine receptors clearly demonstrated no GABAergic synaptic component on LSO principal neurons, suggesting the transmitter subtype switch may be species different. We add a discussion in our revision to clarify this topic.

Reviewer #2 (Recommendations For The Authors):

The data are compelling and report an intriguing functional phenotype. Mechanistic insight into how this phenotype manifests would significantly strengthen this study. For example, which neuroligin is found at these MNTB-LSO synapses?

We agree that investigating the underlying molecular mechanisms, particularly the specific function of each variant of neurexins and their respective ligands on the postsynaptic neurons, is crucial. Exploring these mechanisms, which extend beyond the scope of our current study, would undoubtedly enhance our understanding of neurexin function at various synapses and foster advancements in the field.

Does the TKO alter the ability of MNTB inputs to induce AP firing in LSO neurons?

Activation of the MNTB inputs does not directly induce AP firing in LSO neurons, because the MNTB-LSO synapses are glycinergic and serve to inhibit neuronal activity.

We think the reviewer was to ask whether pan-neurexin deletion in the MNTB neurons alter their ability to impact the firing of LSO neurons. Indeed, the weakening of glycinergic transmission due to pan-neurexin ablation in MNTB neurons could potentially alter the excitation-inhibition (E/I) balance, thereby impacting the overall excitability of LSO neurons. We have conducted preliminary experiments to investigate this aspect and found that the E/I balance at LSO neurons was notably increased in TKO mice. We are currently preparing a manuscript to comprehensively address the role of neurexins at the auditory circuit and behavior levels.

Additional calcium measurements using GECIs would provide insight into whether nanodomain calcium or total calcium is altered at these synapses.

We appreciate the valuable suggestion provided by the reviewer. However, distinguishing between Ca2+ nanodomain and Ca2+ microdomain using Ca2+ imaging techniques requires advanced systems such as two-photon STED microscopy, which are beyond the scope of our current research.

It is unclear why fluorescence intensity is quantified instead of the number of synaptic clusters in LSO. In addition to changes in synapse numbers, fluorescent intensity can indicate a number of other possible morphological changes.

We appreciate the valuable suggestion from the reviewer. We have re-analyzed our imaging data to compare synaptic density. The results, as included in Fig.3f and 3h, confirm an increase in the number of glycinergic synapses after pan-neurexin deletion.

The most robust synaptic phenotypes were produced by measuring light-evoked oIPSCs and the authors acknowledge that electrically-evoked eIPSCs might be contaminated by uninfected fibers or by other sources of glycinergic inputs. I suggest that IPSC PPRs, EGTA, and low Ca2+ experiments be performed using optogenetics.

As discussed in our response to Public Reviews, we acknowledge that optogenetic stimulation offers crucial advantages, and we have provided a balanced discussion of the caveats associated with both methods in our manuscript. Additionally, following the reviewer’s suggestion, we have conducted new optogenetic experiments specifically for measuring the paired-pulse ratio in control and Nrxn123 TKO mice. We included this new dataset in supplementary Figure S2, which is consistent with our result obtained with electrically fiber stimulation.

For experiments involving EGTA and low Ca2+ manipulations, we opted for electrical stimulation due to major concerns regarding potential side effects of optogenetics, including the phototoxicity and photobleaching during prolonged light exposure.

It is sometimes confusing which type of evoked stimulation is being used (e.g. PPR, EGTA, and low Ca2+ experiments). To aid in the interpretations of these experiments, it would help to clarify.

We appreciate the reviewer's suggestion regarding the clarity of the evoked stimulation methods used in our experiments. We have revised the manuscript to provide clearer descriptions of the specific types of evoked stimulation employed in each experiment. Thank you for guiding towards this clarification.

The comparisons to Chen et al 2017 and the senior author's 2020 paper seem disjointed and do not contribute to the findings, which alone, are quite interesting. Given the prevailing notion that neurexins control different synaptic properties depending on the brain region and/or synapse studied, is it surprising that the findings observed here differ from previous studies of different synapses (glutamatergic and GABAergic)?

By comparing previous studies at different types of neurons/synapses, our findings reveal a commonality in the underlying mechanisms of synaptic regulation mediated by neurexins. This convergence of mechanisms across different synapse types highlights the fundamental role of neurexins in synaptic function and plasticity. In addition, this comparative perspective may shed light on the complex interplay between excitatory and inhibitory neurotransmission, which is crucial for maintaining the balance of neuronal activity and network dynamics.

Despite Nrxn3 being the most abundant Nrxn mRNA in MNTB neurons, the possible contributions of this highly expressed protein are not discussed.

We thank the reviewer for bringing up this important point. The differential expression of individual neurexins indeed suggests that specific neurexins may play dominant roles in regulating synaptic transmission. While our study primarily focused on the collective impact of ablating all neurexins, we acknowledge the significance of exploring the specific contributions of individual neurexin isoforms in the future. Understanding the distinct roles of each neurexin isoform could provide valuable insights into the precise mechanisms underlying synaptic function and plasticity. We have added discussion in our revised manuscript Line223-230.

Reviewer #3 (Recommendations For The Authors):

• There are several instances of spaces missing and typos, please carefully check the manuscript.

We greatly appreciate the reviewer's helpful feedback on the text that could be clarified or improved. We have meticulously edited the manuscript to address these concerns.

• While studying the properties of IPSC, apart from optogenetic stimulation, the authors performed experiments with electrical fiber stimulation. Their findings showed a slightly significant reduction of the IPSC amplitude and no effect on the IPSCs kinetics when comparing the TKO and control. One weakness is the discrepancy between the results from the optogenetic and fiber stimulation experiments, which the authors contribute to inefficient transfection in the fiber stimulation experiments. The authors state that they tried to optimize their protocols for virus injection protocols. However, they do not elaborate on how the transfection rates could be improved in the discussion section. Moreover, it would be good to further address the reasons for the difference in amplitude between the control IPSCs in the optogenetic and fiber stimulation experiments.

Echoing the suggestion by Reviewer 2 (see above), we acknowledge that optogenetic stimulation offers certain advantages, and we have provided a balanced discussion of the caveats associated with both methods in our manuscript. In addition, we have performed a new set of optogenetic experiment for the paired-pulse ratio measurement in control and Nrxn123 TKO mice and included as a new figure in supplementary figure S2.

For experiments involving EGTA and low Ca2+ manipulations, we opted for electrical stimulation due to major concerns regarding potential side effects of optogenetics, including the phototoxicity and photobleaching during prolonged light exposure.

We added the detail of virus injection strategy that optimized the transfection rates in the method section “To enhance virus infection efficiency, we decreased the dosage per injection while increasing the frequency of injections. Additionally, we ensured the pipette remained immobilized for 20-30 seconds to guarantee virus absorption at injection sites. As a result of this strategy, we estimated that the vast majority of MNTB neurons were inoculated by AAVs.” See line288-290.

• Abstract: "ablation of all neurexins in MNTB neurons reduced not only the amplitude but also altered the kinetics of the glycinergic synaptic transmission at LSO neurons."

Changed as suggested.

• Consider revising to "The synaptic dysfunctions primarily resulted from an altered dependence of release on voltage-gated Ca2+ influx."

We appreciate the reviewer's suggestion, which helps improve the clarity of our manuscript. We have revise the phrasing as follows: "The synaptic dysfunctions primarily resulted from an impaired calcium sensitivity of release and a loosened coupling between voltage-gated calcium channels and synaptic vesicles."

• Line 39 should be vertebrates.

Revised as suggested.

• Line 49 it would sound better to say "which further points to the diverse actions of neurexins in specific neurons."

Revised as suggested.

• Line 60 - this paragraph could include information about GABA signaling from the MNTB to the LSO, because on line 113 you mention LSO neurons receive inhibitory GABAergic/glycinergic inputs, but when you do not mention blocking of GABA currents to isolate the glycinergic ones.

We thank the reviewer for the thoughtful and detailed suggestion. We revised the text in line 60 to “In the mature mammalian auditory brainstem” and in line 113, we removed GABAergic to emphasize the nature of glycinergic synapse, particularly in the mouse brainstem where no GABAergic components are found (Fisher et al., 2019).

• Line 72/73 it should be adeno-associated virus; line 73: "combining this with the RNAScope technique" sounds better.

Changed as suggested.

• Line 91 using the RNAScope technique; lines 97, 119 as a control; line 108 the functional organization.<br />

Changed as suggested.

• Line 113 should be a pharmacological approach; line 122 optogenetically evoked.

Changed as suggested.

• Line 132, 160: the control.

Changed as suggested.

• Line 147 thus were infected; line 148 likely to be present but were obscured .

Changed as suggested.

• Line 154 which has been routinely used.

Changed as suggested.

• Line 155 It is not supposed to be Figure 2h but 2i; following that Figure 2i should be 2j; in my opinion, Figure 2i does not display a strong depression for the TKO mice.

Changed as suggested.

• Line 171 a better flow is achieved by saying: together these data show.

Changed as suggested.

• EC50 rather than IC50 of [Ca2+].

Changed as suggested.

• 180 it is better to say "we approached the matter by..."; line 183 while recording;

Changed as suggested.

• Line 203 were much stronger than the effect at control synapses; line 206 tightly clustering.

Changed as suggested.

• Line 212 sounds like they provide evidence for retina and spinal cord as well, should be made clear.

Changed as suggested.

• Line 289 previously.

Changed as suggested.

• Line 295 should be 30 min.

Changed as suggested.

• Line 336, 337 confocal microscope.

Changed as suggested.

• Please provide the number of data points also in figure captions or in the results section.

Added in the captions as suggested.

• Line 533, a better phrasing would be: the blocking effect of 0.2 mM Ca on IPSC amplitude.

Changed as suggested.

• Explain either in the methods or result section how was the EC50 of Ca2+ calculated.

Added in the methods as suggested.

Author response:

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

eLife assessment

This study provides important evidence supporting the ability of a new type of neuroimaging, OPM-MEG system, to measure beta-band oscillation in sensorimotor tasks on 2-14 years old children and to demonstrate the corresponding development changes, since neuroimaging methods with high spatiotemporal resolution that could be used on small children are quite limited. The evidence supporting the conclusion is solid but lacks clarifications about the much-discussed advantages of OPM-MEG system (e.g., motion tolerance), control analyses (e.g., trial number), and rationale for using sensorimotor tasks. This work will be of interest to the neuroimaging and developmental science communities.

We thank the editors and reviewers for their time and comments on our manuscript. We have responded in detail to the comments, on a point-by-point basis, below. Included in our responses (and our revised manuscript) are additional analyses to control for trial count, clarification of the advantages of OPM-MEG, and justification of our use of sensory (as distinct from motor) stimulation. In what follows, our responses are in bold typeface; additions to our manuscript are in bold italic typeface. 

Reviewer #1 (Public Review):

Summary:

Compared with conventional SQUID-MEG, OPM-MEG offers theoretical advantages of sensor configurability (that is, sizing to suit the head size) and motion tolerance (the sensors are intrinsically in the head reference frame). This study purports to be the first to experimentally demonstrate these advantages in a developmental study from age 2 to age 34. In short, while the theoretical advantages of OPM-MEG are attractive - both in terms of young child sensitivity and in terms of motion tolerance - neither was in fact demonstrated in this manuscript. We are left with a replication of SQUID-MEG observations, which certainly establishes OPM-MEG as "substantially equivalent" to conventional technology but misses the opportunity to empirically demonstrate the much-discussed theoretical advantages/opportunities.

Thank you for reviewing our manuscript. We agree that our results demonstrate substantial equivalence with conventional MEG. However, as mentioned by Reviewer 3, most past studies have “focused on older children and adolescents (e.g., 9-15 years old)” whereas our youngest group is 25 years. We believe that by obtaining data of sufficient quality in these age groups, without the need for any restriction of head movement, we have demonstrated the advantage of OPM-MEG. We now have made this clear in our discussion:

“…our primary aim was to test the feasibility of OPM-MEG for neurodevelopmental studies. Our results demonstrate we were able to scan children down to age 2 years, measuring high-fidelity electrophysiological signals and characterising the neurodevelopmental trajectory of beta oscillations. The fact that we were able to complete this study demonstrates the advantages of OPM-MEG over conventional-MEG, the latter being challenging to deploy across such a large age range…”

Strengths:

A replication of SQUID-MEG observations, which certainly establishes OPM-MEG as "substantially equivalent" to conventional technology but misses the opportunity to empirically demonstrate the much-discussed theoretical advantages/opportunities.

As noted above the demonstration of equivalence was one of our primary aims. We have elaborated further on the advantages below.

Weaknesses:

The authors describe 64 tri-axial detectors, which they refer to as 192 channels. This is in keeping with some of the SQUID-MEG description, but possibly somewhat disingenuous. For the scientific literature, perhaps "64 tri-axial detectors" is a more parsimonious description.

The number of channels in a MEG system refers to the number of independent measurements of magnetic field. This, in turn, tells us the number of degrees of freedom in the data that can be exploited by algorithms like signal space separation or beamforming. E.g. the MEGIN (cryogenic) MEG system has 306 channels, 102 magnetometers and 204 planar gradiometers. Sensors are constructed as “triple sensor elements” with one magnetometer and 2 gradiometers (in orthogonal orientations) centred on a single location. In our system, each sensor has three orthogonal metrics of magnetic field which are (by definition) independent. We have 64 such sensors, and therefore 192 independent channels – indeed when implementing algorithms like SSS we have shown we can exploit this number of degrees of freedom.1 192 channels is therefore an accurate description of the system.

A small fraction (<20%) of trials were eliminated for analysis because of "excess interference" - this warrants further elaboration.

We agree that this is an important point. We now state in our methods section:

“…Automatic trial rejection was implemented with trials containing abnormally high variance (exceeding 3 standard deviations from the mean) removed. All experimental trials were also inspected visually by an experienced MEG scientist, to exclude trials with large spikes/drifts that were missed by the automatic approach. In the adult group, there was a significant overlap between automatically and manually detected bad trials (0.7+-1.6 trials were only detected manually). In the children 10.0 +-9.4 trials were only detected manually)…”

We also note that the other reviewers and editor questioned whether the higher rejection rate in children had any bearing on results. This is an extremely important question. In revising the manuscript this has also been taken into account with all data reanalysed with equal trial counts in children and adults. Results are presented in Supplementary Information Section 5.

Figure 3 shows a reduced beta ERD in the youngest children. Although the authors claim that OPMMEG would be similarly sensitive for all ages and that SQUID-MEG would be relatively insensitive to young children, one trivial counterargument that needs to be addressed is that OPM has NOT in fact increased the sensitivity to young child ERD. This can possibly be addressed by analogous experiments using a SQUID-based system. An alternative would be to demonstrate similar sensitivity across ages using OPM to a brain measure such as evoked response amplitude. In short, how does Figure 3 demonstrate the (theoretical) sensitivity advantage of OPM MEG in small heads ?

We completely understand the referees’ point – indeed the question of whether a neuromagnetic effect really changes with age, or apparently changes due to a drop in sensitivity (caused by reduced head size or - in conventional MEG and fMRI - increased subject movement) is a question that can be raised in all neurodevelopmental studies.

Our authors have many years’ experience conducting studies using conventional MEG (including in neurodevelopment) and agreed that the idea of scanning subjects down to age two in conventional MEG would not be practical; their heads are too small and they typically fail to tolerate an environment where they are forced to remain still for long periods. Even if we tried a comparative study using conventional MEG, the likely data exclusion rate would be so high that the study would be confounded. This is why most conventional MEG studies only scan older children and adolescents. For this reason, we cannot undertake the comparative study the reviewer suggests. There are however two reasons why we believe sensitivity is not driving the neurodevelopmental effects that we observe:

Proximity of sensors to the head: 

For an ideal wearable MEG system, the distance between the sensors and the scalp surface (sensor proximity) would be the same regardless of age (and size), ensuring maximum sensitivity in all subjects. To test how our system performed in this regard, we undertook analyses to compute scalp-to-sensor distances. This was done in two ways:

(1) Real distances in our adaptable system: We took the co-registered OPM sensor locations and computed the Euclidean distance from the centre of the sensitive volume (i.e. the centre of the vapour cell) to the closest point on the scalp surface. This was measured independently for all sensors, and an average across sensors calculated. We repeated this for all participants (recall participants wore helmets of varying size and this adaptability should help minimise any relationship between sensor proximity and age).

(2) Simulated distances for a non-adaptable system: Here, the aim was to see how proximity might have changed with age, had only a single helmet size been used. We first identified the single example subject with the largest head (scanned wearing the largest helmet) and extracted the scalpto-sensor distances as above. For all other subjects, we used a rigid body transform to co-register their brain to that of the example subject (placing their head (virtually) inside the largest helmet). Proximity was then calculated as above and an average across sensors calculated. This was repeated for all participants.

In both analyses, sensor proximity was plotted against age and significant relationships probed using Pearson correlation. 

In addition, we also wanted to probe the relation between sensor proximity and head circumference. Head circumference was estimated by binarising the whole head MRI (to delineate volume of the head), and the axial slice with the largest circumference around was selected. We then plotted sensor proximity versus head circumference, for both the real (adaptive) and simulated (nonadaptive) case (expecting a negative relationship – i.e. larger heads mean closer sensor proximity). The slope of the relationship was measured and we used a permutation test to determine whether the use of adaptable helmets significantly lowered the identified slope (i.e. do adaptable helmets significantly improve sensor proximity in those with smaller head circumference).

Results are shown in Figure R1. We found no measurable relationship between sensor proximity and age (r = -0.195; p = 0.171) in the case of the real helmets (panel A). When simulating a non-adaptable helmet, we did see a significant effect of age on scalp-to-sensor distance (r = -0.46; p = 0.001; panel B). This demonstrates the advantage of the adaptability of OPM-MEG; without the ability to flexibly locate sensors, we would have a significant confound of sensor proximity. 

Plotting sensor proximity against head circumference we found a significant negative relationship in both cases (r = -0.37; p = 0.007 and  r = -0.78; p = 0.000001); however, the difference between slopes was significant according to a permutation test (p < 0.025) suggesting that adaptable has indeed improved sensor proximity in those with smaller head circumference. This again shows the benefits of adaptability to head size.

Author response image 1.

Scalp-to-sensor distance as a function of age (A/B) and head circumference (C/D). A and C show the case for the real helmets; B and D show the simulated non-adaptable case.

In sum, the ideal wearable system would see sensors located on the scalp surface, to get as close as possible to the brain in all subjects. Our system of multiple helmet sizes is not perfect in this regard (there is still a significant relationship between proximity and head circumference). However, our solution has offered a significant improvement over a (simulated) non-adaptable system. Future systems should aim to improve even further on this, either by using additively manufactured bespoke helmets for every subject (this is a gold standard, but also costly for large studies), or potentially adaptable flexible helmets.

Burst amplitudes:

The reviewer suggested to “demonstrate similar sensitivity across ages using OPM to a brain measure”. We decided not to use the evoked response amplitude (as suggested), since this would be expected to change with age. Instead, we used the amplitude of the bursts.

Our manuscript shows a significant correlation between beta modulation and burst probability – implying that the stimulus-related drop in beta amplitude occurs because bursts are less likely to occur. Further, we showed significant age-related changes in both beta amplitude and burst probability leading to a conclusion that the age dependence of beta modulation was caused by changes in the likelihood of bursts (i.e. bursts are less likely to ’switch off’ during sensory stimulation in children). We have now extended these analyses to test whether burst amplitude also changes significantly with age – we reasoned that if burst amplitude remained the same in children and adults, this would not only suggest that beta modulation is driven by burst probability (distinct from burst amplitude), but also show directly that the beta effects we see are not attributable to a lack of sensitivity in younger people. 

We took the (unnormalized) beamformer projected electrophysiological time series from sensorimotor cortex and filtered it 5-48 Hz (the motivation for the large band was because bursts are known to be pan-spectral and have lower frequency content in children; this band captures most of the range of burst frequencies highlighted in our spectra). We then extracted the timings of the bursts, and for each burst took the maximum projected signal amplitude. These values were averaged across all bursts in an individual subject, and plotted for all subjects against age.

Author response image 2.

Beta burst amplitude as a function of age; A) shows index finger simulation trials; B shows little finger stimulation trials. In both case there was no significant modulation of burst amplitude with age.

Results (see Figure R2) showed that the amplitude of the beta burst showed no significant age-related modulation (R2 = 0.01, p = 0.48 for index finger and R2 = 0.01, p = 0.57 for the little finger). This is distinct from both burst probability and task induced beta modulation. This adds weight to the argument that the diminished beta modulation in children is not caused by a lack of sensitivity to the MEG signal and supports our conclusion that burst probability is the primary driver of the agerelated changes in beta oscillations.

Both of the above analyses have been added to our supplementary information and mentioned in the main manuscript. The first shows no confound of sensor proximity to the scalp with age in our study. The second shows that the bursts underlying the beta signal are not significantly lower amplitude in children – which we reasoned they would be if sensitivity was diminished at younger ages. We believe that the two together suggest that we have mitigated a sensitivity confound in our study.

The data do not make a compelling case for the motion tolerance of OPM-MEG. Although an apparent advantage of a wearable system, an empirical demonstration is still lacking. How was motion tracked in these participants?

We agree that this was a limitation of our experiment. 

We have the equipment to track motion of the head during an experiment, using IR retroreflective markers placed on the helmet and a set of IR cameras located inside the MSR. However, the process takes a long time to set up, it lacks robustness, and would have required an additional computer (the one we typically use was already running the somatosensory stimulus and video). When the study was designed, we were concerned that the increased set up time for motion tracking would cause children to get bored, and result in increased participant drop out. For this reason we decided not to capture motion of the head during this study.

With hindsight this was a limitation which – as the reviewer states – makes us unable to prove that motion robustness was a significant advantage for this study. That said, during scanning there was both a parent and an experimenter in the room for all of the children scanned, and anecdotally we can say that children tended to move their head during scans – usually to talk to the parent. Whilst this cannot be quantified (and is therefore unsatisfactory) we thought it worth mentioning in our discussion, which reads:

“…One limitation of the current study is that practical limitations prevented us from quantitatively tracking the extent to which children (and adults) moved their head during a scan. Anecdotally however, experimenters present in the room during scans reported several instances where children moved, for example to speak to their parents who were also in the room. Such levels of movement could not be tolerated in conventional MEG or MRI and so this again demonstrates the advantages afforded by OPM-MEG…”

As a note, empirical demonstrations of the motion tolerance of OPM-MEG have been published previously: Early demonstrations included Boto et al. 2 who captured beta oscillations in adults playing a ball game and Holmes et al. who measured visual responses as participants moved their head to change viewing angle3. In more recent demonstrations, Seymour et al. measured the auditory evoked field in standing mobile participants4; Rea et al. measured beta modulation as subjects carried out a naturalistic handwriting task5 and Holmes et al measured beta modulation as a subject walked around a room.6

Furthermore, while the introduction discusses at some length the phenomenon of PMBR, there is no demonstration of the recording of PMBR (or post-sensory beta rebound). This is a shame because there is literature suggesting an age-sensitivity to this, that the optimal sensitivity of OPM-MEG might confirm/refute. There is little evidence in Figure 3 for adult beta rebound. Is there an explanation for the lack of sensitivity to this phenomenon in children/adolescents? Could a more robust paradigm (button-press) have shed light on this?

We understand the question. There are two limitations to the current study in respect to measuring the PMBR:

Firstly, sensory tasks generally do not induce as strong a PMBR as motor tasks and with this in mind a stronger rebound response could have been elicited using a button press. However, it was our intention to scan children down to age 2 and we were sceptical that the youngest children would carry out a button press as instructed. For this reason we opted for entirely passive stimulation, requiring no active engagement from our participants. The advantages of this was a stimulus that all subjects could engage with. However, this was at the cost of a diminished rebound.

The second limitation relates to trial length. Multiple studies have shown that the PMBR can last over ~10 s 7,8. Indeed, Pfurtscheller et al. argued in 1999 that it was necessary to leave 10 s between movements to allow the PMBR to return to a true baseline9, though this has rarely been adhered to in the literature. Here, we wanted to keep recordings short for the comfort of the younger participants, so we adopted a short trial duration. However, a consequence of this short trial length is that it becomes impossible to access the PMBR directly; one can only measure beta modulation with the task. This limitation has now been addressed explicitly in our discussion:

“…this was the first study of its kind using OPM-MEG, and consequently aspects of the study design could have been improved. Firstly, the task was designed for children; it was kept short while maximising the number of trials (to maximise signal to noise ratio). However, the classical view of beta modulation includes a PMBR which takes ~10 s to reach baseline following task cessation7–9. Our short trial duration therefore doesn’t allow the rebound to return to baseline between trials, and so conflates PMBR with rest. Consequently, we cannot differentiate the neural generators of the task induced beta power decrease and the PMBR; whilst this helped ensure a short, child friendly task, future studies should aim to use longer rest windows to independently assess which of the two processes is driving age related changes…”

Data on functional connectivity are valuable but do not rely on OPM recording. They further do not add strength to the argument that OPM MEG is more sensitive to brain activity in smaller heads - in fact, the OPM recordings seem plagued by the same insensitivity observed using conventional systems.

Given the demonstration above that bursts are not significantly diminished in amplitude in children relative to adults; and further given the demonstrations in the literature (e.g. Seedat et al.10) that functional connectivity is driven by bursts, we would argue that the effects of connectivity changing with age are not related to sensitivity but rather genuinely reflect a lack of coordination of brain activity.

The discussion of burst vs oscillations, while highly relevant in the field, is somewhat independent of the OPM recording approach and does not add weight to the OPM claims.

We agree that the burst vs. oscillations discussion does not add weight to the OPM claims per se. However, we had two aims of our paper, the second being to “investigate how task-induced beta modulation in the sensorimotor cortices is related to the occurrence of pan-spectral bursts, and how the characteristics of those bursts change with age.” As the reviewer states, this is highly relevant to the field, and therefore we believe adds impact, not only to the paper, but also by extension to the technology.

In short, while the theoretical advantages of OPM-MEG are attractive - both in terms of young child sensitivity and in terms of motion tolerance, neither was in fact demonstrated in this manuscript. We are left with a replication of SQUID-MEG observations, which certainly establishes OPM-MEG as "substantially equivalent" to conventional technology but misses the opportunity to empirically demonstrate the much-discussed theoretical advantages/opportunities.

We thank the referee for the time and important contributions to this paper. We believe the fact that we were able to record good data in children as young as two years old was, in itself, an experimental realisation of the ‘theoretical advantages’ of OPM-MEG. Our additional analyses, inspired by the reviewers comments, help to clarify the advantages of OPM-MEG over conventional technology. The reviewers’ insights have without doubt improved the paper.

Reviewer #2 (Public Review):

Summary:

The authors introduce a new 192-channel OPM system that can be configured using different helmets to fit individuals from 2 to 34 years old. To demonstrate the veracity of the system, they conduct a sensorimotor task aimed at mapping developmental changes in beta oscillations across this age range. Many past studies have mapped the trajectory of beta (and gamma) oscillations in the sensorimotor cortices, but these studies have focused on older children and adolescents (e.g., 9-15 years old) and used motor tasks. Thus, given the study goals, the choice of a somatosensory task was surprising and not justified. The authors recorded a final sample of 27 children (2-13 years old) and 24 adults (21-34 years) and performed a time-frequency analysis to identify oscillatory activity. This revealed strong beta oscillations (decreases from baseline) following the somatosensory stimulation, which the authors imaged to discern generators in the sensorimotor cortices. They then computed the power difference between 0.3-0.8 period and 1.0-1.5 s post-stimulation period and showed that the beta response became stronger with age (more negative relative to the stimulation period). Using these same time windows, they computed the beta burst probability and showed that this probability increased as a function of age. They also showed that the spectral composition of the bursts varied with age. Finally, they conducted a whole-brain connectivity analysis. The goals of the connectivity analysis were not as clear as prior studies of sensorimotor development have not conducted such analyses and typically such whole-brain connectivity analyses are performed on resting-state data, whereas here the authors performed the analysis on task-based data. In sum, the authors demonstrate that they can image beta oscillations in young children using OPM and discern developmental effects.

Thank you for this summary and for taking the time to review our manuscript.

Strengths:

Major strengths of the study include the novel OPM system and the unique participant population going down to 2-year-olds. The analyses are also innovative in many respects.

Thank you – we also agree that the major strength is in the unique cohort.

Weaknesses:

Several weaknesses currently limit the impact of the study. 

First, the choice of a somatosensory stimulation task over a motor task was not justified. The authors discuss the developmental motor literature throughout the introduction, but then present data from a somatosensory task, which is confusing. Of note, there is considerable literature on the development of somatosensory responses so the study could be framed with that.

We completely understand the referee’s point, and we agree that the motivation for the somatosensory task was not made clear in our original manuscript.

Our choice of task was motivated completely by our targeted cohort; whilst a motor task would have been our preference, it was generally felt that making two-year-olds comply with instructions to press a button would have been a significant challenge. In addition, there would likely have been differences in reaction times. By opting for a passive sensory stimulation we ensured compliance, and the same stimulus for all subjects. We have added text on this to our introduction as follows:

“…Here, we combine OPM-MEG with a burst analysis based on a Hidden Markov Model (HMM) 10–12 to investigate beta dynamics. We scanned a cohort of children and adults across a wide age range (upwards from 2 years old). Because of this, we implemented a passive somatosensory task which can be completed by anyone, regardless of age…”

We also state in our discussion:

“…here we chose to use passive (sensory) stimulation. This helped ensure compliance with the task in subjects of all ages and prevented confounds of e.g. reaction time, force, speed and duration of movement which would be more likely in a motor task.7,8 However, there are many other systems to choose and whether the findings here regarding beta bursts and the changes with age also extend to other brain networks remains an open question.…”

Regarding the neurodevelopmental literature – we are aware of the literature on somatosensory evoked responses – particularly median nerve stimulation – but we can find little on the neurodevelopmental trajectory of somatosensory induced beta oscillations (the topic of our paper). We have edited our introduction as follows:

“…All these studies probed beta responses to movement execution; in the case of tactile stimulation (i.e. sensory stimulation without movement) both task induced beta power loss, and the post stimulus rebound have been consistently observed in adults9,13–18. Further, beta amplitude in sensory cortex has been related to attentional processes19 and is broadly thought to carry top down top down influence on primary areas20. However, there is less literature on how beta modulation changes with age during purely sensory tasks.…”

We would be keen for the reviewer to point to any specific papers in the literature that we may have missed.

Second, the primary somatosensory response actually occurs well before the time window of interest in all of the key analyses. There is an established literature showing mechanical stimulation activates the somatosensory cortex within the first 100 ms following stimulation, with the M50 being the most robust response. The authors focus on a beta decrease (desynchronization) from 0.3-0.8 s which is obviously much later, despite the primary somatosensory response being clear in some of their spectrograms (e.g., Figure 3 in older children and adults). This response appears to exhibit a robust developmental effect in these spectrograms so it is unclear why the authors did not examine it. This raises a second point; to my knowledge, the beta decrease following stimulation has not been widely studied and its function is unknown. The maps in Figure 3 suggest that the response is anterior to the somatosensory cortex and perhaps even anterior to the motor cortex. Since the goal of the study is to demonstrate the developmental trajectory of well-known neural responses using an OPM system, should the authors not focus on the best-understood responses (i.e., the primary somatosensory response that occurs from 0.0-0.3 s)?

We understand the reviewer’s point. The original aim of our manuscript was to investigate the neurodevelopmental trajectory of beta oscillations, not the evoked response. In fact, the evoked response in this paradigm is complicated by the fact that there are three stimuli in a very short (<500 ms) time window. For this reason, we prefer the focus of our paper to remain on oscillations.

Nevertheless, we agree that not including the evoked responses was a missed opportunity.  We have now added evoked responses to our analysis pipeline and manuscript. As surmised by the reviewer, the M50 shows neurodevelopmental changes (an increase with age). Our methods section has been updated accordingly and Figure 3 has been modified. The figure and caption are copied below for the convenience of the reviewer.

Author response image 3.

Beta band modulation with age: (A) Brain plots show slices through the left motor cortex, with a pseudo-T-statistical map of beta modulation (blue/green) overlaid on the standard brain. Peak MNI coordinates are indicated for each subgroup. Time frequency spectrograms show modulation of the amplitude of neural oscillations (fractional change in spectral amplitude relative to the baseline measured in the 2.5-3 s window). Vertical lines indicate the time of the first braille stimulus. In all cases results were extracted from the location of peak beta desynchronisation (in the left sensorimotor cortex). Note the clear beta amplitude reduction during stimulation. The inset line plots show the 4-40 Hz trial averaged phase-locked evoked response, with the expected prominent deflections around 20 and 50 ms. (B) Maximum difference in beta-band amplitude (0.3-0.8 s window vs 1-1.5 s window) plotted as a function of age (i.e., each data point shows a different participant; triangles represent children, circles represent adults). Note significant correlation (𝑅2 \= 0.29, 𝑝 = 0.00004 *). (C) Amplitude of the P50 component of the evoked response plotted against age. There was no significant correlation (𝑅2 \= 0.04, 𝑝 = 0.14 ). All data here relate to the index finger stimulation; similar results are available for the little finger stimulation in Supplementary Information Section 1.

Regarding the developmental effects, the authors appear to compute a modulation index that contrasts the peak beta window (.3 to .8) to a later 1.0-1.5 s window where a rebound is present in older adults. This is problematic for several reasons. First, it prevents the origin of the developmental effect from being discerned, as a difference in the beta decrease following stimulation is confounded with the beta rebound that occurs later. A developmental effect in either of these responses could be driving the effect. From Figure 3, it visually appears that the much later rebound response is driving the developmental effect and not the beta decrease that is the primary focus of the study. Second, these time windows are a concern because a different time window was used to derive the peak voxel used in these analyses. From the methods, it appears the image was derived using the .3-.8 window versus a baseline of 2.5-3.0 s. How do the authors know that the peak would be the same in this other time window (0.3-0.8 vs. 1.0-1.5)? Given the confound mentioned above, I would recommend that the authors contrast each of their windows (0.3-0.8 and 1.0-1.5) with the 2.5-3.0 window to compute independent modulation indices. This would enable them to identify which of the two windows (beta decrease from 0.3-0.8 s or the increase from 1.0-1.5 s) exhibited a developmental effect. Also, for clarity, the authors should write out the equation that they used to compute the modulation index. The direction of the difference (positive vs. negative) is not always clear.

We completely understand the referee’s point; referee 1 made a similar point. In fact, there are two limitations of our paradigm regarding the measurement of PMBR versus the task-induced beta decrease:

Firstly, sensory tasks generally do not induce as strong a PMBR as motor tasks and with this in mind a stronger rebound response could have been elicited using a button press. However, as described above it was our intention to scan children down to age 2 and we were sceptical that the youngest children would carry out a button press as instructed.

The second limitation relates to trial length. Multiple studies have shown that the PMBR can last over ~10 s7,8. Indeed, Pfurtscheller et al. argued in 1999 that it was necessary to leave 10 s between movements to allow the PMBR to return to a true baseline9 Here, we wanted to keep recordings relatively short for the younger participants, and so we adopted a short trial duration. However, a consequence of this short trial length is that it becomes impossible to access the PMBR directly because the PMBR of the nth trial is still ongoing when the (n+1)th trial begins. Because of this, there is no genuine rest period, and so the stimulus induced beta decrease and subsequent rebound cannot be disentangled. This limitation has now been made clear in our discussion as follows:

“…this was the first study of its kind using OPM-MEG, and consequently aspects of the study design could have been improved. Firstly, the task was designed for children; it was kept short while maximising the number of trials (to maximise signal to noise ratio). However, the classical view of beta modulation includes a PMBR which takes ~10 s to reach baseline following task cessation7–9. Our short trial duration therefore doesn’t allow the rebound to return to baseline between trials, and so conflates PMBR with rest. Consequently, we cannot differentiate the neural generators of the task induced beta power decrease and the PMBR; whilst this helped ensure a short, child friendly task, future studies should aim to use longer rest windows to independently assess which of the two processes is driving age related changes…”

To clarify our method of calculating the modulation index, we have added the following statement to the methods:

“The beta modulation index was calculated using the equation , where , and are the average Hilbert-envelope-derived amplitudes in the stimulus (0.3-0.8s), post-stimulus (1-1.5s) and baseline (2.5-3s) windows, respectively.”

Another complication of using a somatosensory task is that the literature on bursting is much more limited and it is unclear what the expectations would be. Overall, the burst probability appears to be relatively flat across the trial, except that there is a sharp decrease during the beta decrease (.3-.8 s). This matches the conventional trial-averaging analysis, which is good to see. However, how the bursting observed here relates to the motor literature and the PMBR versus beta ERD is unclear.

Again, we agree completely; a motor task would have better framed the study in the context of existing burst literature – but as mentioned above, making 2-year-olds comply with the instructions for a motor task would have been difficult. Interestingly in a recent paper, Rayson et al. used EEG to investigate burst activity in infants (9 and 12 months) and adults during observed movement execution, with results showing stimulus induced decrease in beta burst rate at all ages, with the largest effects in adults21. This paper was not yet published when we submitted our article but does help us to frame our burst results since there is strong agreement between their study and ours. We now mention this study in both our introduction and discussion. 

Another weakness is that all participants completed 42 trials, but 19% of the trials were excluded in children and 9% were excluded in adults. The number of trials is proportional to the signal-to-noise ratio. Thus, the developmental differences observed in response amplitude could reflect differences in the number of trials that went into the final analyses.

This is an important observation and we thank the reviewer for raising the issue. We have now re-analysed all of our data, removing trials in the adults such that the overall number of trials was the same as for the children. All effects with age remained significant. We chose to keep the Figures in the main manuscript with all good trials (as previously) and present the additional analyses (with matched trial numbers) in supplementary information. However, if the reviewer feels strongly, we could do it the other way around (there is very little difference between the results).

Reviewer #3 (Public Review):

This study demonstrated the application of OPM-MEG in neurodevelopment studies of somatosensory beta oscillations and connections with children as young as 2 years old. It provides a new functional neuroimaging method that has a high spatial-temporal resolution as well wearable which makes it a new useful tool for studies in young children. They have constructed a 192-channel wearable OPM-MEG system that includes field compensation coils which allow free head movement scanning with a relatively high ratio of usable trials. Beta band oscillations during somatosensory tasks are well localized and the modulation with age is found in the amplitude, connectivity, and panspectral burst probability. It is demonstrated that the wearable OPM-MEG could be used in children as a quite practical and easy-to-deploy neuroimaging method with performance as good as conventional MEG. With both good spatial (several millimeters) and temporal (milliseconds) resolution, it provides a novel and powerful technology for neurodevelopment research and clinical applications not limited to somatosensory areas.

We thank the reviewer for their summary, and their time in reviewing our manuscript.

The conclusions of this paper are mostly well supported by data acquired under the proper method. However, some aspects of data analysis need to be improved and extended.

(1) The colour bars selected for the pseudo-T-static pictures of beta modulation in Figures 2 and 3, which are blue/black and red/black, are not easily distinguished from the anatomical images which are grey-scale. A colour bar without black/white would make these figures better. The peak point locations are also suggested to be marked in Figure 2 and averaged locations in Figure 3 with an error bar.

Thank you for this comment which we certainly agree with. The colour scheme used has now been changed to avoid black. We have also added peak locations. 

(2) The data points in plots are not constant across figures. In Figures 3 and 5, they are classified into triangles and circles for children and adults, but all are circles in Figures 4 and 6.

Thank you! We apologise for the confusion. Data points are now consistent across plots.

(3) Although MEG is much less susceptible to conductivity inhomogeneity of the head than EEG, the forward modulating may still be impacted by the small head profile. Add more information about source localization accuracy and stability across ages or head size.

This is an excellent point. We have added to our discussion relating to the accuracy of the forward model. 

“…We failed to see a significant difference in the spatial location of the cortical representations of the index and little finger; there are three potential reasons for this. First, the system was not designed to look for such a difference – sensors were sparsely distributed to achieve whole head coverage (rather than packed over sensory cortex to achieve the best spatial resolution in one area22). Second, our “pseudo-MRI” approach to head modelling (see Methods) is less accurate than acquisition of participantspecific MRIs, and so may mask subtle spatial differences. Third, we used a relatively straightforward technique for modelling magnetic fields generated by the brain (a single shell forward model). Although MEG is much less susceptible to conductivity inhomogeneity of the head than EEG, the forward model may still be impacted by the small head profile. This may diminish spatial resolution and future studies might look to implement more complex models based on e.g. finite element modelling23. Finally, previous work 24 suggested that, for a motor paradigm in adults, only the beta rebound, and not the power reduction during stimulation, mapped motortopically. This may also be the case for purely sensory stimulation. Nevertheless, it remains the case that by placing sensors closer to the scalp, OPM-MEG should offer improved spatial resolution in children and adults; this should be the topic of future work…”

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

Major items to further test include the differing number of trials, the windowing issue, and the focus on motor findings in the intro and discussion. First, I would recommend the authors adjust the number of trials in adults to equate them between groups; this will make their developmental effects easier to interpret.  

Thank you for raising this important point. This has now been done and appears in our supplementary information as discussed above.

Second, to discern which responses are exhibiting developmental effects, the authors need to contrast the 0.3-0.8 window with the later window (2.5-3.0), not the window that appears to have the PMBR-like response. This artificially accentuates the response. I also think they should image the 1.0-1.5 vs 2.5-3.0s window to determine whether the response in this time window is in the same location as the decrease and then contrast this for beta differences. 

We completely understand this point, which relates to separating the reduction in beta amplitude during stimulation and the rebound post stimulation. However, as explained above, doing so unambiguously would require the use of much longer trials. Here we were only able to measure stimulus induced beta modulation (distinct from the separate contributions of the task induced beta power reduction and rebound). It may be that future studies, with >10 s trial length, could probe the role of the PMBR, but such studies require long paradigms which are challenging to implement with children.

Third, changing the framing of the study to highlight the somatosensory developmental literature would also be an improvement.

We have added to our introduction a stated in the responses above.

Finally, the connectivity analysis on data from a somatosensory task did not make sense given the focus of the study and should be removed in my opinion. It is very difficult to interpret given past studies used resting state data and one would expect the networks to dynamically change during different parts of the current task (i.e., stimulation versus baseline).

We appreciate the point regarding connectivity. However, it was our intention to examine the developmental trajectory of beta oscillations, and a major role of beta oscillations is in mediating connectivity. It is true that most studies are conducted in the resting state (or more recently – particularly in children – during movie watching). The fact that we had a sensory task running is a confound; nevertheless, the connectivity we derived in adults bears a marked similarity to that from previous papers (e.g. 25) and we do see significant changes with age. We therefore believe this to be an important addition to the paper and we would prefer to keep it.

References

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Author response:

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

eLife assessment

This important study investigates the transcriptional changes in neurons that underlie loss of learning and memory with age in C. elegans, and how cognition is maintained in insulin/IGF-1-like signaling mutants. The presented evidence is convincing, utilizing a cutting-edge method to isolate neurons from worms for genomics that is clearly conveyed with a rigorous experimental approach. Overall, this study supports that older daf-2 worms maintain cognitive function via mechanisms that are unique from younger wild type worms, which will be of interest to neuroscientists and researchers studying ageing.

Thank you, we appreciate the positive comments.

Public Reviews: 

Reviewer #1 (Public Review): 

The authors perform RNA-seq on FACS-isolated neurons from adult worms at days 1 and 8 of adulthood to profile the gene expression changes that occur with cognitive decline. Supporting data are included indicating that by day 7 of adulthood, learning and memory are reduced, indicating that this time point or after represents cognitively aged worms. Neuronal identity genes are reduced in expression within cognitively aged worms, whereas genes involved in proteostasis, transcription/chromatin, and stress response are elevated. A number of specific examples are provided, representing markers of specific neuronal subtypes, and correlating expression changes to the erosion of particular functions (e.g. motor neurons, chemosensory neurons, aversive learning neurons, etc). 

To investigate whether the upregulation of genes in neurons with age is compensatory or deleterious, the authors reduced the expression of a set of three significantly upregulated genes and performed behavioral assays in young adults. In each case, reduction of expression improved memory, consistent with a model in which age-associated increases impair neuronal function. This claim would be bolstered by an experiment elevating the expression of these genes in young neurons, which should reduce the learning index if the hypothesis is correct. 

This is an interesting suggestion. Our long-term goal is to find ways to improve memory, and to better understand the “rules” that might govern changes with age. In this case, were interested in addressing the hypothesis that genes that rise with age must be compensatory, which is a frequently stated theory that is not often tested. Here we showed that knocking down three genes that are upregulated in aged animals improved memory; our results suggest that the wild-type functions of these genes are likely deleterious for learning and memory functions, and further, that their increased expression with age is not a compensatory function. Certainly for future work, it might be interesting to better understand how and why these specific genes have a deleterious function that increases with age, and whether that function is different in younger animals where they are not highly expressed.

The authors then characterize learning and memory in wild-type, daf-2, and daf-2/daf-16 worms with age and find that daf-2 worms have an extended ability to learn for approximately 10 days longer than wild types. This was daf-16 dependent. Memory was extended in daf-2 as well, and strikingly, daf-2;daf-16 had no short-term memory even at day 1. Transcriptomic analysis of FACS-sorted neurons was performed on the three groups at day 8. The authors focus their analysis on daf-2 vs. daf-2;daf-16 and present evidence that daf-2 neurons express a stress-resistance gene program. One question that remains unanswered is how well the N2 and daf-2;daf-16 correlate overall, and are there differences? This may be informative as wild type and daf-2;daf-16 mutants are not phenotypically identical when it comes to memory, and there may be differences that can be detected despite the overlap in the PCA. This analysis could reveal the daf-16 targets involved in memory. 

Re. daf-2;daf-16 vs N2: This is a good suggestion. Our analysis in Fig. S5 showed that the daf-2 vs N2 comparison shows similar results with the daf-2 vs daf-16;daf-2 comparison, but some additional genes are differentially expressed. Interestingly, the daf-2 vs N2 comparison shows that the bZip transcription factors are upregulated in daf-2 compared with N2 worms (Fig. S6f). This may indicate that additional transcription factors are controlled by the daf-2 mutation in the nervous system in addition to the DAF-16/FOXO transcription factor.

Author response image 1.

We also identified the differentially expressed genes in the Day 8 neuronal daf-16;daf-2 to N2 comparison, as the reviewer is asking about. The samples from different genotypes do separate from one another in the PCA plot, indicating there are differences between daf-16,daf-2 and N2 neurons. However, the difference is smaller and there are fewer genes differentially expressed between daf-16;daf-2 and N2: only 38 genes are significantly higher in daf-16;daf-2, and only 53 genes are significantly higher in N2 (log2FC > 0.5, p-adj<0.05). The genes higher in N2 are enriched in endopeptidase inhibitors, and the genes higher in daf-16;daf-2 are not enriched in any gene ontology terms. These results indicate that there are some differences between daf-16;daf-2 and N2 neurons, which correlates with the behavioral differences we see, but the difference is small compared to daf-2 neurons. We have added these data to the paper (Fig. S4e,f); thank you for the suggestion.

The authors tested eight candidate genes that were more highly expressed in daf-2 neurons vs. daf-2;daf-16 and showed that reduction of 2 and 5 of these genes impaired learning and memory, respectively, in daf-2 worms. This finding implicates specific neuronal transcriptional targets of IIS in maintaining cognitive ability in daf-2 with age, which, importantly, are distinct from those in young wild type worms. 

Reviewer #2 (Public Review): 

Weng et al. perform a comprehensive study of gene expression changes in young and old animals, in wild-type and daf-2 insulin receptor mutants, in the whole animal, and specifically in the nervous system. Using this data, they identify gene families that are correlated with neuronal ageing, as well as a distinct set of genes that are upregulated in neurons of aged daf-2 mutants. This is particularly interesting as daf-2 mutants show both extended lifespans and healthier neurons in aged animals, reflected by better learning/memory in older animals compared with wild-type controls. Indeed, the knockdown of several of these upregulated genes resulted in poorer learning and memory. In addition, the authors showed that several genes upregulated during ageing in wild-type neurons also contribute to learning and memory; specifically knockdown of these genes in young animals resulted in improved memory. This indicates that (at least in this small number of cases), genes that show increased transcript levels with age in the nervous system somehow suppress memory, potentially by having damaging effects on neuronal health. 

Finally, from a resource perspective, the neuronal transcriptome provided here will be very useful for C. elegans researchers as it adds to other existing datasets by providing the transcriptome of older animals (animals at day 8 of adulthood) and demonstrating the benefits of performing tissue-specific RNAseq instead of whole-animal sequencing. 

Thank you!

The work presented here is of high quality and the authors present convincing evidence supporting their conclusions.

Thanks!

I only have a few comments/suggestions: 

(1) Do the genes identified to decrease learning/memory capacity in daf-2 animals (Figure 4d/e) also impact neuronal health? daf-2 mutant worms show delayed onset of age-related changes to neuron structure (Tank et al., 2011, J Neurosci). Does knockdown of the genes shown to affect learning also affect neuron structure during ageing, potentially one mechanism through which they modulate learning/memory? 

Thank you for this suggestion, which would be good for a future direction, particularly for genes that might have some relationship to previously-identified cellular structural process. The genes we tested here include dod-24, alh-2, mtl-1, F08H9,4, C44B7.5, hsp-12.3, hsp-12.6, and cpi-1, which are related to stress response, proteolysis inhibitor, metabolic, and innate immunity GO categories, thus associated with stress resistance, proteolysis, lipid metabolism processes; none are obvious choices for morphological effects.

However, it is worth noting that learning and memory decline much faster (Days 4-8) than morphological differences are observed (generally after Day 12-15). Moreover, those morphological differences have been studied primarily in mechanosensory neurons (touch neurons) rather than the chemosensory neurons that are involved in learning and memory, so additional genes may be required for those differences that we were not focusing on in thisi study.

(2) The learning and memory assay data presented in this study uses the butanone olfactory learning paradigm, which is well established by the same group. Have the authors tried other learning assays when testing for learning/memory changes after the knockdown of candidate genes? Depending on the expression pattern of these genes, they may have more or less of an effect on olfactory learning versus for example gustatory or mechanosensory-based learning. 

The reason that we use the butanone olfactory learning paradigm is because it is more similar to learning of information (neutral odorant association with positive cue (food)) – the kind of memory we would like to preserve in humans - rather than a stress-induced memory, such as starvation or pathogenesis-associated aversive learning paradigms, which are more like PTSD. (There is likely to be quite a bit of overlap in mechanism, however, including the role of genes such as magi-1 and casy-1, so it would not be surprising if many of these genes also were required for other learning paradigms.)

(3) I have a comment on the 'compensatory vs dysregulatory' model as stated by the authors on page 7. I understand that this model presents the two main options, but perhaps this is slightly too simplistic: the gene expression that rises during ageing may be detrimental for memory (= dysregulatory), but at the same time may also be beneficial for other physiological roles in other tissues (=compensatory). 

This is a good point, and we made the clarification that in the text: “There may be other scenarios in which a gene with multiple functions may be detrimental for some behaviors but beneficial for other physiological roles.”

Reviewer #3 (Public Review): 

Summary: 

In this manuscript, Weng et al. detect a neuron-specific transcriptome that regulates aging. The authors first profile neuron-specific responses during aging at a time point where a loss in memory function is present. They discover signatures unique to neurons which validate their pipeline and reveal the loss of neuron identity with age. For example, old neurons reduce the expression of genes related to synaptic function and neuropeptide signaling and increase the expression of chromatin regulators, insulin peptides, and glycoproteins. The authors discover the detrimental effect of selected upregulated genes (utx-1, ins-19, and nmgp-1) by knocking them down in the whole body and detecting improvement of short memory functions. They then use their pipeline to test neuronal profiles of long-lived insulin/IGF mutants. They discover that genes related to stress response pathways are upregulated upon longevity (e.g. dod-24, F08H9.4) and that they are required for improved neuron function in long-lived individuals. 

Strengths: 

Overall, the manuscript is well-written, and the experiments are well-described. The authors take great care to explain their reasoning for performing experiments in a specific way and guide the reader through the interpretation of the results, which makes this manuscript an enjoyable and interesting read. Using neuron-specific transcriptomic analysis in aged animals the authors discover novel regulators of learning and memory, which underlines the importance of cell-specific deep sequencing. The time points of the transcriptomic profiling are elegantly chosen, as they coincide with the loss of memory and can be used to specifically reveal gene expression profiles related to neuron function. The authors showcase on the dod-24 example how powerful this approach is. In long-lived insulin/IGF-1 receptor mutants body-wide dod-24 expression differs from neuron-specific profiles. Importantly, the depletion of dod-24 has an opposing effect on lifespan and learning memory. The dataset will provide a useful resource for the C. elegans and aging community. 

Thank you, we do hope people will find the data useful.

Weaknesses: 

While this study nicely describes the neuron-specific profiles, the authors do not test the relevance in a tissue-specific way. It remains unclear if modifying the responses only in neurons has implications for either memory or potentially for lifespan. The authors point to this in the text and refer to tissue-specific datasets. However, it is possible that the tissue-specific profile changes with age. The authors should consider mining publicly available cell-specific aging datasets and performing neuron-specific RNAi to test the functional relevance of the neuron-specific response. This would strengthen the importance of cell-specific profiling.

Thank you for your suggestions. As we have mentioned in the text, our candidate genes are either (1) only expressed in the neurons (alh-2 and F08H9.4), or they are only more highly expressed in daf-2 compared to wild type only in the nervous system (C44B7.5 or dod-24). Thus, the effect we see from knocking down these genes in daf-2 are likely neuron-specific. Additionaly, we performed our assays with neuron-sensitive RNAi strain CQ745: daf-2(e1370) III; vIs69 [pCFJ90(Pmyo-2::mCherry + Punc-119::sid-1)] V. It has been previously shown that neuronal expression of sid-1 decreases non-neuronal RNAi, suggesting that neurons expressing transgenic sid-1(+) served as a sink for dsRNA (Calixto et al., 2010). Thus, this neuron-sensitive RNAi is likely neuron-specific and our results is unlikely from knocking down these genes in non-neuronal tissues. However, we do acknowledge this issue.

To identify the expression pattern of these genes in a more cell-specific way in the adults, we examined the expression of our candidate genes that affected learning and memory, namely dod-24, F08H9.4, C44B7.9, alh-2, and mtl-1, in the Calico database (Roux et al., 2023). From that database, we can see that dod-24 is mainly expressed in the PHC and PVM neurons, and F08H9.4 is largely expressed in various neurons. Both have only slight expression outside the nervous system. C44B7.5 and mtl-1 are more broadly expressed, but C44B7.5 was not found to be differentially expressed in other tissues in daf-2, and mtl-1 only had a slight effect on learning and memory. Perhaps due to their sequencing depth and detection limit, Roux et al. didn’t detect alh-2 expression anywhere in their data.

Thus, the neuron-specific expression and daf-2 differential expression pattern of these genes indicate that the learning and memory improvement in aged daf-2 is unlikely due to neuronal non-autonomous effects.

To better address this concern (that for the genes that we found only expressed in the neurons, the neuron-confined expression may change with age) we examined the expression pattern change of these genes with age. As is shown below, from the Calico database, we can see that the expression in the nervous system persists, and even slightly increases, with age, thus age-related expression pattern change is not a concern to our analysis.

Author response image 2.

Author response image 3.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Most of my comments are in the public section. A few additional recommendations for the authors regarding the formatting/presentation: 

The presentation of Figure S6e-h in the introduction is somewhat confusing and feels out of order. If presented first, it should be S1. Otherwise, discussion of this figure should go at the end of the results section or in the discussion if appropriate. 

Thank you for pointing this out. We have moved the discussion of this figure to the Discussion section.

I do not see Figure S5 described in the text.

Good catch, thank you. We have added the descriptions for Figure S5 in the text.

In general, check the figures, figure legends, and how they are referenced in the text, particularly the supplemental figures and legends.

Minor comments:

There is a typo in the Figure 4 legend: Neuronal IIX should be IIS. 

Thanks for pointing this out. We have corrected it in the text.

Reviewer #2 (Recommendations For The Authors): 

• There are multiple instances throughout the manuscript where there are statements in brackets that provide justification or explanation for some of the approaches used. There is no reason for 'side note' brackets to be used. I suggest removing them and incorporating these statements into the narrative.

Thank you, we have now incorporated these points into the main text.

• Introduction: page 4 "here we RNA-sequenced FACS-isolated neurons" should be "here we performed RNA sequencing on FACS-isolated neurons...".

Thank you, we have changed the text accordingly.

• Figure 2A: I do not understand the legend for this panel "Tissue Query for wild-type genes expressed at higher levels in aged worms show lower nervous system and neuron prediction score." Please clarify.

We have clarified the Figure 2A legend:

(A)  Tissue prediction score for wild-type genes expressed at higher levels in aged worms.

• Page 8: "We previously observed that loss of single genes that play a role in complex behaviors like learning and memory can have a large impact on function 60, unlike the additive roles of longevity-promoting genes 11." - a large impact on what function?

Thank you for noting, we have clarified it in the text accordingly:

“We previously observed that for genes that play a role in complex behaviors like learning and memory, the loss of single genes can have a large impact on these complex behaviors 60, unlike the additive roles of longevity-promoting genes 11.”

• Next line "Therefore, one mechanism by which wild-type worms lose their function with age..." - again, what function?

Thank you for noting this, we have clarified the text to say we refer to the learning and memory functions.

• Page 9: "Thus, daf-2 mutants maintain their higher cognitive quality of life longer than wild-type worms, while daf-16;daf-2 mutants spend their whole lives without memory ability (Figure 3d), in contrast to claims that daf-2 mutants are less healthy than wild-type or daf-16 worms23." - since ref 23 did not perform any learning/memory tests, the definition of 'health' in ref 23 is different to 'cognitive health' as studied here. So the findings in this study are not 'in contrast' to ref 23 but rather add to these findings.

Learning and memory ability is an important function for a healthy individual, thus we would assert that indeed, cognitive health is an important part of the “health” of daf-2 worms. In ref 23, Bansal et al. claim that daf-2 worms are less healthy without assessing their learning and memory ability; their lack of data is an insufficient reason for us to remove our statement, as cognitive health is part of healthspan. Here we find that the “learning span” of daf-2 lasts at least proportionally if not longer than that of wild type. We have also previously shown that daf-2 worms also have longer maximum velocity span with age (Hahm et al., 2015), in direct contrast with Bansal et al.’s claim that daf-2 worms move less well and thus are less healthy – daf-2 worms simply stop sooner when presented with food and switch to feeding, due to their higher odr-10 levels. The Bansal paper continues to be frequently cited as finding that daf-2 mutants are less healthy than wild type, a claim for which we can still find no experimental evidence to support. Therefore, it is important that we make the point that daf-2 worms have extended cognitive health, which is part of health span.

• Page 13: I feel like the sentence "Furthermore, memory maintenance with age might require additional functions that were not previously uncovered in analyses of young animals" is both vague (what functions are referred to?) and a little bit obvious (obvious that age-related changes would not be revealed in analyses of young animals). Perhaps rephrase to make the desired point clearer? 

We have clarified the sentence in the text:

“Furthermore, memory maintenance with age might require additional genes that function in promoting stress resistance and neuronal resilience, which were not previously uncovered in analyses of young animals.”

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Protein conformational changes are often critical to protein function, but obtaining structural information about conformational ensembles is a challenge. Over a number of years, the authors of the current manuscript have developed and improved an algorithm, qFit protein, that models multiple conformations into high resolution electron density maps in an automated way. The current manuscript describes the latest improvements to the program, and analyzes the performance of qFit protein in a number of test cases, including classical statistical metrics of data fit like Rfree and the gap between Rwork and Rfree, model geometry, and global and case-by-case assessment of qFit performance at different data resolution cutoffs. The authors have also updated qFit to handle cryo-EM datasets, although the analysis of its performance is more limited due to a limited number of high-resolution test cases and less standardization of deposited/processed data.

Strengths:

The strengths of the manuscript are the careful and extensive analysis of qFit's performance over a variety of metrics and a diversity of test cases, as well as the careful discussion of the limitations of qFit. This manuscript also serves as a very useful guide for users in evaluating if and when qFit should be applied during structural refinement.

Reviewer #2 (Public Review):

Summary

The manuscript by Wankowicz et al. describes updates to qFit, an algorithm for the characterization of conformational heterogeneity of protein molecules based on X-ray diffraction of Cryo-EM data. The work provides a clear description of the algorithm used by qFit. The authors then proceed to validate the performance of qFit by comparing it to deposited X-ray entries in the PDB in the 1.2-1.5 Å resolution range as quantified by Rfree, Rwork-Rfree, detailed examination of the conformations introduced by qFit, and performance on stereochemical measures (MolProbity scores). To examine the effect of experimental resolution of X-ray diffraction data, they start from an ultra high-resolution structure (SARS-CoV2 Nsp3 macrodomain) to determine how the loss of resolution (introduced artificially) degrades the ability of qFit to correctly infer the nature and presence of alternate conformations. The authors observe a gradual loss of ability to correctly infer alternate conformations as resolution degrades past 2 Å. The authors repeat this analysis for a larger set of entries in a more automated fashion and again observe that qFit works well for structures with resolutions better than 2 Å, with a rapid loss of accuracy at lower resolution. Finally, the authors examine the performance of qFit on cryo-EM data. Despite a few prominent examples, the authors find only a handful (8) of datasets for which they can confirm a resolution better than 2.0 Å. The performance of qFit on these maps is encouraging and will be of much interest because cryo-EM maps will, presumably, continue to improve and because of the rapid increase in the availability of such data for many supramolecular biological assemblies. As the authors note, practices in cryo-EM analysis are far from uniform, hampering the development and assessment of tools like qFit.

Strengths

qFit improves the quality of refined structures at resolutions better than 2.0 A, in terms of reflecting true conformational heterogeneity and geometry. The algorithm is well designed and does not introduce spurious or unnecessary conformational heterogeneity. I was able to install and run the program without a problem within a computing cluster environment. The paper is well written and the validation thorough.

I found the section on cryo-EM particularly enlightening, both because it demonstrates the potential for discovery of conformational heterogeneity from such data by qFit, and because it clearly explains the hurdles towards this becoming common practice, including lack of uniformity in reporting resolution, and differences in map and solvent treatment.

Weaknesses

The authors begin the results section by claiming that they made "substantial improvement" relative to the previous iteration of qFit, "both algorithmically (e.g., scoring is improved by BIC, sampling of B factors is now included) and computationally (improving the efficiency and reliability of the code)" (bottom of page 3). However, the paper does not provide a comparison to previous iterations of the software or quantitation of the effects of these specific improvements, such as whether scoring is improved by the BIC, how the application of BIC has changed since the previous paper, whether sampling of B factors helps, and whether the code faster. It would help the reader to understand what, if any, the significance of each of these improvements was.

Indeed, it is difficult (embarrassingly) to benchmark against our past work due to the dependencies on different python packages and the lack of software engineering. With the infrastructure we’ve laid down with this paper, made possible by an EOSS grant from CZI, that will not be a problem going forward. Not only is the code more reliable and standardized, but we have developed several scientific test sets that can be used as a basis for broad comparisons to judge whether improvements are substantial. We’ve also changed with “substantial improvement” to “several modifications”  to indicate the lack of comparison to past versions.

The exclusion of structures containing ligands and multichain protein models in the validation of qFit was puzzling since both are very common in the PDB. This may convey the impression that qFit cannot handle such use cases. (Although it seems that qFit has an algorithm dedicated to modeling ligand heterogeneity and seems to be able to handle multiple chains). The paper would be more effective if it explained how a user of the software would handle scenarios with ligands and multiple chains, and why these would be excluded from analysis here.

qFit can indeed handle both. We left out multiple chains for simplicity in constructing a dataset enriched for small proteins while still covering diversity to speed the ability to rapidly iterate and test our approaches. Improvements to qFit ligand handling will be discussed in a forthcoming work as we face similar technical debt to what we saw in proteins and are undergoing a process of introducing “several modifications” that we hope will lead to “substantial improvement” - but at the very least will accelerate further development.

It would be helpful to add some guidance on how/whether qFit models can be further refined afterwards in Coot, Phenix, ..., or whether these models are strictly intended as the terminal step in refinement.

We added to the abstract:

“Importantly, unlike ensemble models, the multiconformer models produced by qFit can be manually modified in most major model building software (e.g. Coot)  and fit can be further improved by refinement using standard pipelines (e.g. Phenix, Refmac, Buster).”

and introduction:

“Multiconformer models are notably easier to modify and more interpretable in software like Coot12 unlike ensemble methods that generate multiple complete protein copies(Burnley et al. 2012; Ploscariu et al. 2021; Temple Burling and Brünger 1994).”

and results:

“This model can then be examined and edited in Coot12 or other visualization software, and further refined using software such as phenix.refine, refmac, or buster as the modeler sees fit.”

and discussion

“qFit is compatible with manual modification and further refinement as long as the subsequent software uses the PDB standard altloc column, as is common in most popular modeling and refinement programs. The models can therefore generally also be deposited in the PDB using the standard deposition and validation process.”

Appraisal & Discussion

Overall, the authors convincingly demonstrate that qFit provides a reliable means to detect and model conformational heterogeneity within high-resolution X-ray diffraction datasets and (based on a smaller sample) in cryo-EM density maps. This represents the state of the art in the field and will be of interest to any structural biologist or biochemist seeking to attain an understanding of the structural basis of the function of their system of interest, including potential allosteric mechanisms-an area where there are still few good solutions. That is, I expect qFit to find widespread use.

Reviewer #3 (Public Review):

Summary:

The authors address a very important issue of going beyond a single-copy model obtained by the two principal experimental methods of structural biology, macromolecular crystallography and cryo electron microscopy (cryo-EM). Such multiconformer model is based on the fact that experimental data from both these methods represent a space- and time-average of a huge number of the molecules in a sample, or even in several samples, and that the respective distributions can be multimodal. Different from structure prediction methods, this approach is strongly based on high-resolution experimental information and requires validated single-copy high-quality models as input. Overall, the results support the authors' conclusions.

In fact, the method addresses two problems which could be considered separately:

- An automation of construction of multiple conformations when they can be identified visually;

- A determination of multiple conformations when their visual identification is difficult or impossible.

We often think about this problem similarly to the reviewer. However, in building qFit, we do not want to separate these problems - but rather use the first category (obvious visual identification) to build an approach that can accomplish part of the second category (difficult to visualize) without building “impossible”/nonexistent conformations - with a consistent approach/bias.

The first one is a known problem, when missing alternative conformations may cost a few percent in R-factors. While these conformations are relatively easy to detect and build manually, the current procedure may save significant time being quite efficient, as the test results show.

We agree with the reviewers' assessment here. The “floor” in terms of impact is automating a tedious part of high resolution model building and improving model quality.

The second problem is important from the physical point of view and has been addressed first by Burling & Brunger (1994; https://doi.org/10.1002/ijch.199400022). The new procedure deals with a second-order variation in the R-factors, of about 1% or less, like placing riding hydrogen atoms, modeling density deformation or variation of the bulk solvent. In such situations, it is hard to justify model improvement. Keeping Rfree values or their marginal decreasing can be considered as a sign that the model is not overfitted data but hardly as a strong argument in favor of the model.

We agree with the overall sentiment of this comment. What is a significant variation in R-free is an important question that we have looked at previously (http://dx.doi.org/10.1101/448795) and others have suggested an R-sleep for further cross validation (https://pubmed.ncbi.nlm.nih.gov/17704561/). For these reasons it is important to get at the significance of the changes to model types from large and diverse test sets, as we have here and in other works, and from careful examination of the biological significance of alternative conformations with experiments designed to test their importance in mechanism.

In general, overall targets are less appropriate for this kind of problem and local characteristics may be better indicators. Improvement of the model geometry is a good choice. Indeed, yet Cruickshank (1956; https://doi.org/10.1107/S0365110X56002059) showed that averaged density images may lead to a shortening of covalent bonds when interpreting such maps by a single model. However, a total absence of geometric outliers is not necessarily required for the structures solved at a high resolution where diffraction data should have more freedom to place the atoms where the experiments "see" them.

Again, we agree—geometric outliers should not be completely absent, but it is comforting when they and model/experiment agreement both improve.

The key local characteristic for multi conformer models is a closeness of the model map to the experimental one. Actually, the procedure uses a kind of such measure, the Bayesian information criteria (BIC). Unfortunately, there is no information about how sharply it identifies the best model, how much it changes between the initial and final models; in overall there is not any feeling about its values. The Q-score (page 17) can be a tool for the first problem where the multiple conformations are clearly separated and not for the second problem where the contributions from neighboring conformations are merged. In addition to BIC or to even more conventional target functions such as LS or local map correlation, the extreme and mean values of the local difference maps may help to validate the models.

We agree with the reviewer that the problem of “best” model determination is poorly posed here. We have been thinking a lot about htis in the context of Bayesian methods (see: https://www.ncbi.nlm.nih.gov/pmc/articles/PMC9278553/); however, a major stumbling block is in how variable representations of alternative conformations (and compositions) are handled. The answers are more (but by no means simply) straightforward for ensemble representations where the entire system is constantly represented but with multiple copies.

This method with its results is a strong argument for a need in experimental data and information they contain, differently from a pure structure prediction. At the same time, absence of strong density-based proofs may limit its impact.

We agree - indeed we think it will be difficult to further improve structure prediction methods without much more interaction with the experimental data.

Strengths:

Addressing an important problem and automatization of model construction for alternative conformations using high-resolution experimental data.

Weaknesses:

An insufficient validation of the models when no discrete alternative conformations are visible and essentially missing local real-space validation indicators.

While not perfect real space indicators, local real-space validation is implicit in the MIQP selection step and explicit when we do employ Q-score metrics.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

A point of clarification: I don't understand why waters seem to be handled differently in for cryo-EM and crystallography datasets. I am interested about the statement on page 19 that the Molprobity Clashscore gets worse for cryo-EM datasets, primarily due to clashes with waters. But the qFit algorithm includes a round of refinement to optimize placement of ordered waters, and the clashscore improves for the qFit refinement in crystallography test cases. Why/how is this different for cryo-EM?

We agree that this was not an appropriate point. We believe that the high clash score is coming from side chains being incorrectly modeled. We have updated this in the manuscript and it will be a focus of future improvements.

Reviewer #2 (Recommendations For The Authors):

- It would be instructive to the reader to explain how qFit handles the chromophore in the PYP (1OTA) example. To this end, it would be helpful to include deposition of the multiconformer model of PYP. This might also be a suitable occasion for discussion of potential hurdles in the deposition of multiconformer models in the PDB (if any!). Such concerns may be real concerns causing hesitation among potential users.

Thank you for this comment. qFit does not alter the position or connectivity of any HETATM records (like the chromophore in this structure). Handling covalent modifications like this is an area of future development.

Regarding deposition, we have noted above that the discussion now includes:

“qFit is compatible with manual modification and further refinement as long as the subsequent software uses the PDB standard altloc column, as is common in most popular modeling and refinement programs. The models can therefore, generally also be deposited in the PDB using the standard deposition and validation process.”

Finally, we have placed all PDBs in a Zenodo deposition (XXX) and have included that language in the manuscript. It is currently under a separate data availability section (page XXX). We will defer to the editor as to the best header that should go under.

- It may be advisable to take the description of true/false pos/negatives out of the caption of Figure 4, and include it in a box or so, since these terms are important in the main text too, and the caption becomes very cluttered.

We think adding the description of true/false pos/negatives to the Figure panel would make it very cluttered and wordy. We would like to retain this description within the caption. We have also briefly described each in the main text.

- page 21, line 4: some issue with citation formatting.

We have updated these citations.

- page 25, second paragraph: cardinality is the number of members of a set. Perhaps "minimal occupancy" is more appropriate.

Thank you for pointing this out. This was a mistake and should have been called the occupancy threshold.

- page 26: it's - its

Thank you, we have made this change. 

- Font sizes in Supplementary Figures 5-7 are too small to be readable.

We agree and will make this change. 

Reviewer #3 (Recommendations For The Authors):

General remarks

(1) As I understand, the procedure starts from shifting residues one by one (page 4; A.1). Then, geometry reconstruction (e.g., B1) may be difficult in some cases joining back the shifted residues. It seems that such backbone perturbation can be done more efficiently by shifting groups of residues ("potential coupled motions") as mentioned at the bottom of page 9. Did I miss its description?

We would describe the algorithm as sampling (which includes minimal shifts) in the backbone residues to ensure we can link neighboring residues. We agree that future iterations of qFit should include more effective backbone sampling by exploring motion along the Cβ-Cα, C-N, and (Cβ-Cα × C-N) bonds and exploring correlated backbone movements.

(2) While the paper is well split in clear parts, some of them seem to be not at their right/optimal place and better can be moved to "Methods" (detailed "Overview of the qFit protein algorithm" as a whole) or to "Data" missed now (Two first paragraphs of "qFit improves overall fit...", page 8, and "Generating the qFit test set", page 22, and "Generating synthetic data ..." at page 26; description of the test data set), At my personal taste, description of tests with simulated data (page 15) would be better before that of tests with real data.

Thank you for this comment, but we stand by our original decision to keep the general flow of the paper as it was submitted.

(3) I wonder if the term "quadratic programming" (e.g., A3, page 5) is appropriate. It supposes optimization of a quadratic function of the independent parameters and not of "some" parameters. This is like the crystallographic LS which is not a quadratic function of atomic coordinates, and I think this is a similar case here. Whatever the answer on this remark is, an example of the function and its parameters is certainly missed.

We think that the term quadratic programming is appropriate. We fit a function with a loss function (observed density - calculated density), while satisfying the independent parameters. We fit the coefficients minimizing a quadratic loss. We agree that the quadratic function is missing from the paper, and we have now included it in the Methods section.

Technical remarks to be answered by the authors :

(1) Page 1, Abstract, line 3. The ensemble modeling is not the only existing frontier, and saying "one of the frontiers" may be better. Also, this phrase gives a confusing impression that the authors aim to predict the ensemble models while they do it with experimental data.

We agree with this statement and have re-worded the abstract to reflect this.

(2) Page 2. Burling & Brunger (1994) should be cited as predecessors. On the contrary, an excellent paper by Pearce & Gros (2021) is not relevant here.

While we agree that we should mention the Burling & Brunger paper and the Pearce & Gros (2021) should not be removed as it is not discussing the method of ensemble refinement.

(3) Page 2, bottom. "Further, when compared to ..." The preference to such approach sounds too much affirmative.

We have amended this sentence to state:

“Multiconformer models are notably easier to modify and more interpretable in software like Coot(Emsley et al. 2010) unlike ensemble methods that generate multiple complete protein copies(Burnley et al. 2012; Ploscariu et al. 2021; Temple Burling and Brünger 1994).”

“The point we were trying to make in this sentence was that ensemble-based models are much harder to manually manipulate in Coot or other similar software compared to multiconformer models. We think that the new version of this sentence states this point more clearly.”

(4) Page 2, last paragraph. I do not see an obvious relation of references 15-17 to the phrase they are associated with.

We disagree with this statement, and think that these references are appropriate.

“Multiconformer models are notably easier to modify and more interpretable in software like Coot12 unlike ensemble methods that generate multiple complete protein copies(Burnley et al. 2012; Ploscariu et al. 2021; Temple Burling and Brünger 1994).”

(5) Page 3, paragraph 2. Cryo-EM maps should be also "high-resolution"; it does not read like this from the phrase.

We agree that high-resolution should be added, and the sentence now states:

“However, many factors make manually creating multiconformer models difficult and time-consuming. Interpreting weak density is complicated by noise arising from many sources, including crystal imperfections, radiation damage, and poor modeling in X-ray crystallography, and errors in particle alignment and classification, poor modeling of beam induced motion, and imperfect detector Detector Quantum Efficiency (DQE) in high-resolution cryo-EM.”

(6) Page 3, last paragraph before "results". The words "... in both individual cases and large structural bioinformatic projects" do not have much meaning, except introducing a self-reference. Also, repeating "better than 2 A" looks not necessary.

We agree that this was unnecessary and have simplified the last sentence to state:

“With the improvements in model quality outlined here, qFit can now be increasingly used for finalizing high-resolution models to derive ensemble-function insights.”

(7) Page 3. "Results". Could "experimental" be replaced by a synonym, like "trial", to avoid confusing with the meaning "using experimental data"?

We have replaced experimental with exploratory to describe the use of qFit on CryoEM data. The statement now reads:

“For cryo-EM modeling applications, equivalent metrics of map and model quality are still developing, rendering the use of qFit for cryo-EM more exploratory.”

(8) Page 4, A.1. Should it be "steps +/- 0.1" and "coordinate" be "coordinate axis"? One can modify coordinates and not shift them. I do not understand how, with the given steps, the authors calculated the number of combinations ("from 9 to 81"). Could a long "Alternatively, ...absent" be reduced simply to "Otherwise"?

We have simplified and clarified the sentence on the sampling of backbone coordinates to state:

“If anisotropic B-factors are absent, the translation of coordinates occurs in the X, Y, and Z directions. Each translation takes place in steps of 0.1 along each coordinate axis, extending to 0.3 Å, resulting in 9 (if isotropic) or to 81 (if anisotropic) distinct backbone conformations for further analysis.”

(9) Page 6, B.1, line 2. Word "linearly" is meaningless here.

We have modified this to read:

“Moving from N- to C- terminus along the protein,”

(10) Page 9, line 2. It should be explained which data set is considered as the test set to calculate Rfree.

We think this is clear and would be repetitive if we duplicated it.

(11) Page 9, line 7. It should be "a valuable metric" and not "an"

We agree and have updated the sentence to read:

“Rfree is a valuable metric for monitoring overfitting, which is an important concern when increasing model parameters as is done in multiconformer modeling.”

(12) Page 10, paragraph 3. "... as a string (Methods)". I did not find any other mention of this term "string", including in "Methods" where it supposed to be explained. Either this should be explained (and an example is given?), or be avoided.

We agree that string is not necessary (discussing the programmatic datatype). We have removed this from the sentence. It now reads:

“To quantify how often qFit models new rotameric states, we analyzed the qFit models with phenix.rotalyze, which outputs the rotamer state for each conformer (Methods).”

(13) Page10, lines 3-4 from bottom. Are these two alternative conformations justified?

We are unsure what this is referring to.

(14) Page 12, Fig. 2A. In comparison with Supplement Fig 2C, the direction of axes is changed. Could they be similar in both Figures?

We have updated Supplementary Figure 2C to have the same direction of axes as Figure 2A.

(15) Page 15, section's title. Choose a single verb in "demonstrate indicate".

We have amended the title of this section to be:

“Simulated data demonstrate qFit is appropriate for high-resolution data.”

(16) Page 15, paragraph 2. "Structure factors from 0.8 to 3.0 A resolution" does not mean what the author wanted apparently to tell: "(complete?) data sets with the high-resolution limit which varied from 0.8 to 3.0 A ...". Also, a phrase of "random noise increasing" is not illustrated by Figs.5 as it is referred to.

We have edited this sentence to now read:

“To create the dataset for resolution dependence, we used the ground truth 7KR0 model, including all alternative conformations, and generated artificial structure factors with a high resolution limit ranging from  0.8 to 3.0 Å resolution (in increments of 0.1 Å).”

(17) Page 15, last paragraph is written in a rather formal and confusing way while a clearer description is given in the figure legend and repeated once more in Methods. I would suggest to remove this paragraph.

We agree that this is confusing. Instead of create a true positive/false positive/true negative/false negative matrix, we have just called things as they are, multiconformer or single conformer and match or no match. We have edited the language the in the manuscript and figure legends to reflect these changes.

(18) Page 16. Last two paragraphs start talking about a new story and it would help to separate them somehow from the previous ones (sub-title?).

We agree that this could use a subtitle. We have included the following subtitle above this section:

“Simulated multiconformer data illustrate the convergence of qFit.”

(19) Page 20. "or static" and "we determined that" seem to be not necessary.

We have removed static and only used single conformer models. However, as one of the main conclusions of this paper is determining that qFit can pick up on alternative conformers that were modeled manually, we have decided to the keep the “we determined that”.

(20) Page 21, first paragraph. "Data" are plural; it should be "show" and "require"

We have made these edits. The sentence now reads:

“However, our data here shows that not only does qFit need a high-resolution map to be able to detect signal from noise, it also requires a very well-modeled structure as input.”

(21) Page 21, References should be indicated as [41-45], [35,46-48], [55-57]. A similar remark to [58-63] at page 22.

We have fixed the reference layout to reflect this change.

(22) Page 21, last paragraph. "Further reduce R-factors" (moreover repeated twice) is not correct neither by "further", since here it is rather marginal, nor as a goal; the variations of R-factors are not much significant. A more general statement like "improving fit to experimental data" (keeping in mind density maps) may be safer.

We agree with the duplicative nature of these statements. We have amended the sentence to now read:

“Automated detection and refinement of partial-occupancy waters should help improve fit to experimental data further reduce Rfree15 and provide additional insights into hydrogen-bond patterns and the influence of solvent on alternative conformations.”

(23) Page 22. Sub-sections of "Methods" are given in a little bit random order; "Parallelization of large maps" in the middle of the text is an example. Put them in a better order may help.

We have moved some section of the Methods around and made better headings by using an underscore to highlight the subsections (Generating and running the qFit test set, qFit improved features, Analysis metrics, Generating synthetic data for resolution dependence).

(24) Page 24. Non-convex solution is a strange term. There exist non-convex problems and functions and not solutions.

We agree and we have changed the language to reflect that we present the algorithm with non-convex problems which it cannot solve.

(25) Page 26, "Metrics". It is worthy to describe explicitly the metrics and not (only) the references to the scripts.

For all metrics, we describe a sentence or two on what each metric describes. As these metrics are well known in the structural biology field, we do not feel that we need to elaborate on them more.

(26) Page 26. Multiplying B by occupancy does not have much sense. A better option would be to refer to the density value in the atomic center as occ*(4*pi/B)^1.5 which gives a relation between these two entities.

We agree and have update the B-factor figures and metrics to reflect this.

(27) Page 40, suppl. Fig. 5. Due to the color choice, it is difficult to distinguish the green and blue curves in the diagram.

We have amended this with the colors of the curves have been switched.

(28) Page 42, Suppl. Fig. 7. (A) How the width of shaded regions is defined? (B) What the blue regions stand for? Input Rfree range goes up to 0.26 and not to 0.25; there is a point at the right bound. (C) Bounds for the "orange" occupancy are inversed in the legend.

(A) The width of the shaded region denotes the standard deviations among the values at every resolution. We have made this clearer in the caption

(B) The blue region denotes the confidence interval for the regression estimate. Size of the confidence interval was set to 95%. We have made this clearer in the caption

(C) This has been fixed now

The maximum R-free value is 0.2543, which we rounded down to 0.25.

(29) Page 43. Letters E-H in the legend are erroneously substituted by B-E.

We apologize for this mistake. It is now corrected.

Author response:

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

Reviewer #1 (Comments to the Author):

Summary:

In this study, Xie and colleagues aimed to explore the function and potential mechanisms of the gut microbiota in a hamster model of severe leptospirosis. The results demonstrated that Leptospira infection was able to cause intestine damage and inflammation. Leptospira infection promoted an expansion of Proteobacteria, increased gut barrier permeability, and elevated LPS levels in the serum. Thus, they proposed an LPS-neutralization therapy which improved the survival rate of moribund hamsters combined with antibody therapy or antibiotic therapy.

Strengths:

The work is well-designed and the story is interesting to me. The gut microbiota is essential for immunity and systemic health. Many life-threatening pathogens, such as SARS-CoV-2 and other gut-damaged infection, have the potential to disrupt the gut microbiota in the later stages of infection, causing some harmful gut microbiota-derived substances to enter the bloodstream. It is emphasized that in addition to exogenous pathogenic pathogens, harmful substances of intestinal origin should also be considered in critically ill patients.

Weaknesses:

Q1: There are many serotypes of Leptospira, it is suggested to test another pathogenic serotype of Leptospira to validate the proposed therapy.

That’s a constructive suggestion. We have tested another pathogenic serotype of Leptospira (L. interrogans serovar Autumnalis strain 56606) to verify the LPS-neutralization therapy combined with antibiotic therapy (Supplementary Fig. S9B). The results showed that the combination of the LPS-neutralization therapy with antibody therapy or antibiotic therapy also significantly improved the survival rate of hamsters infected by 56606.

Q2: Authors should explain why the infective doses of leptospires was not consistent in different study.

Thank you for your comment. To examine the role of the gut microbiota on acute leptospirosis, the infective doses of leptospires was chosen for 106, while in other sections of the study, the infective doses of leptospires was chosen for 107. In fact, we also used 107 leptospires to infect hamsters, however, the infective doses of 107 leptospires might be overdose, there was no significant difference on the survival rate between the control group and the Abx-treated group. A previous study also highlighted that the infective doses of leptospires was important in the investigating the sex on leptospirosis, as male hamsters infected with L. interrogans are more susceptible to severe leptospirosis after exposure to lower infectious doses than females (103 leptospires but not 104 leptospires) (1).

Reference

(1) GOMES C K, GUEDES M, POTULA H H, et al. Sex Matters: Male Hamsters Are More Susceptible to Lethal Infection with Lower Doses of Pathogenic Leptospira than Female Hamsters (J). Infect Immun, 2018, 86(10).

Q3: In the discussion section, it is better to supplement the discussion of the potential link between the natural route of infection and leptospirosis.

Thank for your suggestion. We have supplemented it in the discussion (line 523-527 in the track change PDF version).

Q4: Line 231, what is the solvent of thioglycolate?

We have supplemented it in the manuscript (line 242-243 in the track change PDF version).

Q5: Lines 962-964, there are some mistakes which are not matched to Figure 7.

Thank you for pointing that out, we have corrected it in the manuscript.

Reviewer #2 (Comments to the Author):

Summary:

Severe leptospirosis in humans and some mammals often meet death in the endpoint. In this article, authors explored the role of the gut microbiota in severe leptospirosis. They found that Leptospira infection promoted a dysbiotic gut microbiota with an expansion of Proteobacteria and LPS neutralization therapy synergized with antileptospiral therapy significantly improved the survival rates in severe leptospirosis. This study is well-organized and has potentially important clinical implications not only for severe leptospirosis but also for other gut-damaged infections.

Weaknesses:

Q1: In the Introduction section and Discussion section, the authors should describe and discuss more about the differences in the effect of Leptospira infection between mice and hamsters, so that the readers can follow this study better.

Thank you for your suggestion, we have supplemented it in the manuscript (line 62-66 in the track change PDF version).

Q2: Lines 92-95, the authors should explain why they chose two different routines of infection.

Thank you for your comment, we have explained it in the manuscript (line 100 in the track change PDF version).

Q3: Line 179-180, the concentration of PMB and Dox is missed, and 0.016 μg/L is just ok.

We have corrected it in the manuscript.

Q4: "μL" or "μl" and "mL" or "ml' should be uniform in the manuscript.

Thank you for your suggestion, we have revised it in the manuscript.

Q5: In the culture of primary macrophages, how many cells are inoculated in the plates should be described clearly.

We have supplemented it in the manuscript (line 250 in the track change PDF version).

Q6: Line 271, it is better to list primers used for leptospiral detection in the text. Because it allows readers to find the information they need more directly.

Thank you for your suggestions, we have supplemented it in the manuscript (line 281-284 in the track change PDF version).

Q7: Line 366-369, Lactobacillus seems to be a kind of key bacteria during Leptospira infection. A previous study (doi: 10.1371/journal.pntd.0005870) also demonstrated that pre-treatment with Lactobacillus plantarum prevented severe pathogenesis in mice. The authors should discuss the potential probiotic for leptospirosis prevention.

We have discussed it in the manuscript (line 564-566 in the track change PDF version).

Q8: Lines 450-451, not all concentrations of fecal filtration from two groups upregulated all gene expression mentioned in the text, the authors should correct it.

Thank you for pointing that out, we have corrected it in the manuscript (line 461-462 in the track change PDF version).

Reviewer #3 (Comments to the Author):

Summary:

This is a well-prepared manuscript that presented interesting research results. The only defect is that the authors should further revise the English language.

Strengths:

The omics method produced unbiased results.

Weaknesses:

Q1: LPS neutralization is not a new method for treating leptospiral infection.

Thank you for your comment. Yes, LPS neutralization is not a new method for treating leptospiral infection, most of which might focus on leptospiral LPS. In addition, Leptospira seemed to be naturally resistant to polymyxin B (1). Recently, neutralizing gut-derived LPS was applied in other diseases which significantly relieved diseases (2-3). In this study, we found that Leptospira infection promoted an expansion of Proteobacteria, increased gut barrier permeability, and elevated LPS levels in the serum. Thus, we proposed an LPS-neutralization therapy which improved the survival rate of moribund hamsters combined with antibody therapy or antibiotic therapy.

Reference

(1) LIEGEON G, DELORY T, PICARDEAU M. Antibiotic susceptibilities of livestock isolates of leptospira (J). Int J Antimicrob Agents, 2018, 51(5):693-699.

(2) MUNOZ L, BORRERO M J, UBEDA M, et al. Intestinal Immune Dysregulation Driven by Dysbiosis Promotes Barrier Disruption and Bacterial Translocation in Rats With Cirrhosis (J). Hepatology, 2019, 70(3):925-938.

(3) ZHANG X, LIU H, HASHIMOTO K, et al. The gut-liver axis in sepsis: interaction mechanisms and therapeutic potential (J). Crit Care, 2022, 26(1):213.

Q2: The authors should further revise the English language used in the text.

Thank you for your suggestion, our manuscript has been polished by American Journal Experts (certificate number: 81C8-C5C1-9D5D-109D-3F23).

Author response:

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

eLife assessment

In their valuable study, Chen et al. aim to define the neuronal role of HMMR, a microtubule-associated protein typically associated with cell division. Their findings suggest that HMMR is necessary for proper neuronal morphology and the generation of polymerizing microtubules within neurites, potentially by promoting the function of TPX2. While the study is recognized as a first step in deciphering the influence of HMMR on microtubule organization in neurons, reviewers note the current work has important gaps and would benefit from further exploration of the mechanism of microtubule stability by HMMR, the link between HMMR-mediated microtubule generation and morphogenesis, and the physiological implications of disrupting HMMR during neuronal morphogenesis.

Public Reviews:

Reviewer #1 (Public Review):

The microtubule cytoskeleton is essential for basic cell functions, enabling intracellular transport, and establishment of cell polarity and motility. Microtubule-associated proteins (MAPs) contribute to the regulation of microtubule dynamics and stability - mechanisms that are specifically important for the development and physiological function of neurons. Here, the authors aimed to elucidate the neuronal function of the MAP Hmmr, which they had previously identified in a quantitative study of the proteome associated with neuronal microtubules.

The authors conduct well-controlled experiments to demonstrate the localization of endogenous as well as exogenous Hmmr on microtubules within the soma as well as all neurites of hippocampal neurons. Functional analysis using gain- and loss-of-function approaches demonstrates that Hmmr levels are crucial for neuronal morphogenesis, as the length of both dendrites and axons decreases upon loss of Hmmr and increases upon Hmmr overexpression. In addition to length alterations, the branching pattern of neurites changes with Hmmr levels. To uncover the mechanism of how Hmmr influences neuronal morphology, the authors follow the lead that Hmmr overexpression induces looped microtubules in the soma, indicative of an increase in microtubule stability. Microtubule acetylation indeed decreases and increases with Hmmr LOF and GOF, respectively. Together with a rescue of nocodazole-induced microtubule destabilization by Hmmr GOF, these results argue that Hmmr regulates microtubule stability. Highlighted by the altered movement of a plus-end-associated protein, Hmmr also has an effect on the dynamic nature of microtubules. The authors present evidence suggesting that the nucleation frequency of neuronal microtubules depends on Hmmr's ability to recruit the microtubule nucleator Tpx2. Together, these data add novel insight into MAP-mediated regulation of microtubules as a prerequisite for neuronal morphogenesis. While the data shown support the author's conclusions, the study also has several weaknesses:

• The study appears incomplete as the initial proteomics analysis which is referenced as an entry into the study is not presented. This surely is the authors' choice, however, without presenting this data set, it would make more sense if the authors first showed the localization of Hmmr on neuronal microtubules and then started with the functional analysis.

The reviewer suggests moving the Hmmr localization data in front of the loss- and gain-of-function data because we did not present the proteomics data. However, we still believe placing the loss- and gain-of-function data in the beginning is the better arrangement. This is because it allows the audience to see the drastic changes on neuronal morphology when HMMR is depleted or overly abundant. It also provides a better linkage between HMMR’s localization on microtubules and its effect on the stability and dynamics of microtubules.

• Neurite branching is quantified, but the methods used are not consistent (normalized branch density vs. Sholl analysis) and there is no distinction between alterations of branching in dendrites vs. axons. This information should be added as it could prove informative with respect to the physiological function of Hmmr in neurite branching.

Sholl analysis is considered the gold standard in neurite branching analyses. However, in the knockdown experiment (Figure 1A~1E), HMMR-depleted neurons exhibited extremely short axons (<100 μm) and dendrites (<40 μm). Using Sholl analysis to assess the branching of these Hmmrdepleted neurons became unsuitable. That is why we used normalized branch density (Figure 1E) in the knockdown experiment and Sholl analysis (Figure 1J) in the overexpression experiment.

Regarding the branching difference between axons and dendrites, only axons exhibit branches at 4 DIV. Therefore, the branching analysis focuses on axons rather than on dendrites. We have revised the manuscript to clarify this.

• The authors show that altered Hmmr levels affect neurite branching and identify an effect on microtubule stability and dynamics as a molecular mechanism. However, how branching correlates with or is regulated by Hmmr-mediated microtubule dynamics is neither addressed experimentally nor discussed by the authors. The physiological significance of altered neuronal morphogenesis also lacks discussion.
• To discuss how branching correlates with or is regulated by HMMR-mediated microtubule dynamics, we have added the following paragraph into the Discussion section:

“It has been shown that compromising microtubule nucleation in neurons by SSNA1 mutant overexpression prevents proper axon branching (Basnet et al., 2018). Additionally, dendritic branching in Drosophila sensory neurons depends on the orientation of microtubule nucleation. Nucleation that results in an anterograde microtubule growth leads to increased branching, while nucleation that results in a retrograde microtubule growth leads to decreased branching (Yalgin et al., 2015). These results demonstrate the importance of microtubule nucleation on neurite branching. It is conceivable that overexpressing a microtubule nucleation promoting protein such as HMMR results in an increase of branching complexity.”

• In terms of discussing the physiological significance of altered neuronal morphogenesis. We have added the following paragraph to the Discussion section:

“Neurons are the communication units of the nervous system. The formation of their intricate shape is therefore crucial for the physiological function. Alterations in neuronal morphogenesis have a profound impact on how nerve cells communicate, leading to a variety of physiological consequences. These consequences include impaired neural circuit formation and function, compromised signal transmission between neurons, as well as altered anatomical structure of the CNS. Depending on the specific type and location of the morphogenetically altered neurons, the physiological consequences can include neurological disorders such as autism spectrum disorder (Berkel et al., 2012) and schizophrenia (Goo et al., 2023), as well as learning and memory deficits (Winkle et al., 2016). However, due to the involvement of HMMR on mitosis, most HMMR mutations are associated with familial cancers (based on ClinVar data).”

• Multiple times, the manuscript lacks a rationale for an experimental approach, choice of cell type, time points, regions of interest, etc. Also, a meaningful description of the methods and for how data were analyzed is missing, making the paper hard to read for someone not directly from the field.

We understand the reviewer’s comments regarding the lack of rationale for choosing the experimental approach, choice of cell type, time points, regions of interest, etc. As a result, we have added the rationales where appropriate to help readers from other fields to better understand the choice of cell type, time points, regions of interest, etc. A brief explanation is shown below:

• Approach and timing: We employed both electroporation (immediate but milder expression) and lipofectamine transfection (delayed but stronger expression). We prioritized knocking down HMMR early in development, so electroporation was used. For overexpression experiments, we chose lipofectamine which allows high protein expression level to be achieved.

• Cell selection: Hippocampal neurons were chosen in experiments that involve morphological quantification due to their homogeneous morphology. On the other hand, cortical neurons were selected in experiments that require large amounts of neurons and/or experiments where we want to demonstrate the universality of a proposed hypothesis.

• Regions of interest (ROIs): In our previous publication (Chen et al., 2017), it was discovered that a significant reduction of EB3 emanation frequency can be detected at the tip and the base of the neurite but not in the middle of the neurite in TPX2-depleted neurons. The reason for this difference is due to the presence of GTP-bound Ran GTPase (RanGTP) at the tip and the base of the neurite. Since RanGTP has also been shown to regulate the interaction between HMMR and TPX2 in the cell-free system (Scrofani et al., 2015), it is possible that the same phenomenon can be observed in HMMR-depleted neurons. This is why we examined those 3 ROIs in Figure 4.

Reviewer #2 (Public Review):

The mechanism of microtubule formation, stabilization, and organization in neurites is important for neuronal function. In this manuscript, the authors examine the phenotype of neurons following alteration in the level of the protein HMMR, a microtubule-associated protein with established roles in mitosis. Neurite morphology is measured as well as microtubule stability and dynamic parameters using standard assays. A binding partner of HMMR, TPX2, is localized. The results support a role for HMMR in neurons.

The work presented in this manuscript seeks to determine if a MAP called HMMR contributes to microtubule dynamics in neurons. Several steps, including validation of the RNAi, additional statistical analysis, use of cells at the same age in culture, and better documentation in figures, would increase the impact of the work.

In many places, the data can be improved which might make the story more convincing. As presented, the results show that HMMR is distributed as puncta on neurons with data coming from a single HMMR antibody, and some background staining that was not discussed. In the discussion the authors state that HMMR impacts microtubule stability, which was evaluated by the presence of post-translational modification and resistance to nocodazole; the data are suggestive but not entirely convincing. The discussion also states that HMMR increases the “amount” of growing microtubules which was measured as the frequency of comet appearance. The authors did not comment on how the number of growing microtubules results in the observed morphological changes.

We actually tested several HMMR antibodies, including E-19 (Santa Cruz, sc-16170), EPR4054 (Abcam, ab124729), and a variety of antibodies provided by Prof. Eva Turley. E-19 performed the best in immunofluorescence (IF) staining and knockdown validation. The other antibodies either failed to detect HMMR in IF staining or generate excessive background signal. We understand that the final images are produced using a single antibody. But since we meticulous validated this antibody and that the localization of overexpressed HMMR is consistent with the endogenous HMMR, we are very confident about our data generated using this single antibody.

We have added the following paragraph in the Discussion section to elucidate how the number of growing microtubules result in the observed morphological changes such as an increase of axon branches:

“It has been shown that compromising microtubule nucleation in neurons by SSNA1 mutant overexpression prevents proper axon branching (Basnet et al., 2018). Additionally, dendritic branching in Drosophila sensory neurons depends on the orientation of microtubule nucleation. Nucleation that results in an anterograde microtubule growth leads to increased branching, while nucleation that results in a retrograde microtubule growth leads to decreased branching (Yalgin et al., 2015). These results demonstrate the importance of microtubule nucleation on neurite branching. It is conceivable that overexpressing a microtubule nucleation promoting protein such as HMMR results in an increase of branching complexity.

Reviewer #1 (Recommendations for The Authors):

(1) The manuscript jumps extensively between main figures and supplementary figures. Please check whether parts of the supplement could be moved to the main figures.

We understand the frustration of moving back and forth between the main figures and supplementary figures. After examining the manuscript, we decided to combine Figure 2A with Figure S3.

(2) In Figure 1, total neurite length between days 3 and 4 DIV does not appear to change - can this be true?

Please check or else explain.

We carefully re-examined our raw data and found out the total neurite length of 4 DIV hippocampal neurons expressing non-targeting shRNA (Figure 1B) and that of 3 DIV hippocampal neurons expressing AcGFP (Figure 1G) are indeed very similar. The explanation is that the 3 DIV hippocampal neurons used for Figure 1G was cultured in low-density and in the presence of cortical neuron-conditioned neurobasal medium (as written in Methods, Neuron culture and transfection section). The low-density culture with minimal overlapping neurites allowed us to better quantify total neurite length, because neurons expressing AcGFP-mHMMR sprouted long and highly branched axons. However, the addition of cortical neuron-conditioned neurobasal medium promoted neurite elongation. This is the reason why the total neurite length of 4 DIV hippocampal neurons expressing non-targeting shRNA (Figure 1B) and that of 3 DIV hippocampal neurons expressing AcGFP (Figure 1G) is similar.

(3) Groen et al. have shown that Hmmr also bundles microtubules, a mechanism that surely is important for neuronal microtubules. Please discuss.

We thank the reviewer for pointing out that HMMR also bundles microtubules and have added this to our revised Discussion section:

“It has been shown that the Xenopus HMMR homolog XRHAMM bundles microtubules in vitro (Groen et al., 2004). In addition, deleting proteins which promote microtubule bundling (e.g., doublecortin knockout, MAP1B/MAP2 double knockout) leads to impaired neurite outgrowth (Bielas et al., 2007; Teng et al., 2001). These observations are consistent with our data that overexpressing HMMR leads to the increased axon and dendrite outgrowth, while depleting it results in the opposite phenotype (Figure 1).”

(4) Please explain why in Figure 4, cortical neurons were chosen for analysis and why and how the three different ROIs were picked.

To answer the question why we chose cortical neurons for the analyses in Figure 4, it will be important to explain why we used hippocampal neurons for other figures. Primary hippocampal neurons have a high homogeneity in terms of their morphology. This uniform morphology allows more consistent morphological quantification. Figure 4, however, does not involve morphological quantification. We are more confident to conclude that HMMR regulates microtubule dynamics if this effect can be detected in the relatively heterogeneous cortical neurons. These are the reasons why we chose to analyze cortical neurons in Figure 4.

In our previous publication (Chen et al., 2017), it was discovered that a significant reduction of EB3 emanation frequency can be detected at the tip and the base of the neurite but not in the middle of the neurite in TPX2-depleted neurons. The reason for this difference is due to the presence of GTP-bound Ran GTPase (RanGTP) at the tip of the neurite and in the soma. Since RanGTP has also been shown to regulate the interaction between HMMR and TPX2 in the cell-free system (Scrofani et al., 2015), it is possible that the same phenomenon can be observed in HMMR-depleted neurons. This was why we examined those 3 ROIs in Figure 4.

(5) Microtubule looping has been shown to occur in regions prior to branch formation (e.g. Dent et al. 2004). As the authors identify increased looping upon Hmmr GOF, this should be discussed.

We thank the reviewer for pointing out that microtubule looping occurs in regions of branch formation and have added this to our revised discussion:

“It is worth noting that the elevated level of HMMR increases the branching density of axons (Figure 1J) and promotes the formation of looped microtubules (Figure 3A). This is consistent with the observations that looped microtubules are often detected in regions of axon branch formation (Dent et al., 1999; Dent and Kalil, 2001; Purro et al., 2008).”

Reviewer #2 (Recommendations for The Authors):

(1) The work seeks to gain insight into microtubule behavior in neurons, an important issue.

(2) Several steps, including validation of the RNAi, additional statistical analysis, use of cells at the same age in culture, and better documentation in figures, would increase the impact of the work.

(3) Figure 1 documents the results of experiments in which the HMMR protein was depleted using shRNA. A western blot of cell extracts from control and depleted cells is needed to verify that the protein level is reduced; alternatively, documentation of the reduction in RNA levels in treated cells could be provided. Neurite, axon, and dendrite length and branch density are measured. The neurite length is in microns, and the axon length is normalized to 100% of the non-treated cells. Please use the same for measures for easier comparison. Looking at the images in Figure 1, the length of the dendrites does not look different in the examples shown, whereas the axon appears shorter. This impression is not supported by the quantification. Are representative images shown? Additionally, the authors should report the values for each replicate of the experiment and compare the three averages rather than comparison of lengths from all measurements. A related issue is that the dendrites do not look longer in panel F, following overexpression of HMMR. For examples of using averages of replicates see: https://pubmed.ncbi.nlm.nih.gov/32346721/

The reviewer mentioned that Western blot of cell extracts or RNA quantification from control and depleted cells are needed to verify that the protein level is reduced.

Unfortunately, these assays are extremely difficult to perform in primary neurons due to the low transfection efficiency. We believe that the consistent knockdown phenotype from 3 different shRNA sequences (Figure 1A-D) and the immunofluorescence staining in depleted primary neurons (Figure S2) are sufficient to confirm that HMMR level is reduced.

We revised Figure 1C, 1D, 1H, 1I so that axon and dendrite lengths are all in micron.

We selected another image for the non-targeting control in Figure 1A to better demonstrate the reduction of dendrite length when HMMR is knocked down.

We thank the reviewer for the suggestion of comparing the three average values rather than comparing all measurements. We have performed statistical analyses for all our data using the average values and revised the graphs accordingly. While the P-values changed, our conclusions remain the same.

We thank the reviewer for pointing out this discrepancy and have selected another image of the AcGFP control for Figure 1F to better demonstrate the increase of dendrite length when HMMR is overexpressed.

(4) Given the changes in neurite morphology, the authors examine the localization of endogenous and overexpressed. The supplemental figures (see S2 and S3) show evidence that HMMR is present in a punctate pattern by conventional immunofluorescence. This is reasonable evidence that the protein is in a linear pattern along cytoskeletal microtubules and that the signal is present in puncta. Please move this to the main text, perhaps replacing Figure 2A, which is low magnification and very hard to see the HMMR staining. Additionally, the level of overexpression of HMMR is not mentioned. Please address this; were cells with similar levels of overexpression selected? Did the result depend on the overexpression? A related issue is the DIV for the cells - some are examined earlier and some at later times; does this impact the results? Please provide information or perform experiments with consistent timing. For the immunofluorescence, were multiple antibodies tried to see if the result was the same with each? Were different fixations, in addition to methanol, utilized?

We have replaced Figure 2A with Figure S3 based on the reviewer’s suggestion.

In the HMMR overexpression experiments, we used HMMR antibody and immunofluorescence staining to confirm that the overexpression is achieved. However, we did not quantify to what extend HMMR was overexpressed.

We performed all the depletion experiments on 4 DIV to maximize knockdown efficiency and performed all the overexpression experiments on 3 DIV to prevent excessive axon fasciculation. Nonetheless, we examined the effect of HMMR depletion on neuronal morphology on 3 DIV. The trend of reduced total neurite length, axon length, and dendrite length can be observed, but no statistical significance can be detected. We also examined the effect of HMMR overexpression on neuronal morphology on 4 DIV and did observe an increase of total neurite length, axon length, and dendrite length. But the overlapping and bundled axons made reliable quantification extremely difficult.

We actually tested multiple HMMR antibodies, such as E-19 (Santa Cruz, sc-16170), EPR4054 (Abcam, ab124729), and a variety of antibodies provided by Prof. Eva Turley. E19 performed the best in immunofluorescence (IF) staining and knockdown validation. The other antibodies either failed to detect HMMR in IF staining or generate excessive background signal. We also tested various fixation methods, including 37°C formaldehyde fixation, -20°C methanol fixation, 37°C formaldehyde followed by -20°C methanol fixation. All fixation methods generated similar IF staining pattern using the E-19 antibody, but 3.7% formaldehyde fixation produced the highest signal.

(5) In Figure 2 C it is hard to see DAPI fluorescence. Are the white areas in the merge with bright cell nuclei? Is Figure 2C control or overexpressing cells? If this is endogenous, is there less signal in PLA compared with S4, which was in culture longer and is overexpressed prior to using PLA for detection?

The white areas in Figure 2C the reviewer mentioned are not cell nuclei, they are actually bubbles formed within the mounting medium.

HMMR detected in Figure 2C is endogenous. We did not quantitatively compare the PLA signals in Figure 2C and those in Figure S4. This is because the PLA signals in Figure 2C are generated using anti-HMMR (to detect endogenous HMMR) and anti-β-III-tubulin antibodies while those in Figure S4 are generated using anti-AcGFP (to detect overexpressed AcGFP-mHMMR) and anti-β-III-tubulin antibodies. Since the affinity of the two antibodies (i.e., anti-HMMR and anti-AcGFP) toward their antigens is different, comparing the PLA signals is not informative.

(6) The images of the endogenous HMMR (Fig S3) and the PLA with tubulin and HMMR antibodies are not the same (2C). The "dots" in PLA are widely separated; gauging from the marker bar length of 50 μm, the small clusters of dots are about 10 μm apart. In Figure S3, the puncta are much more closely spaced, appearing almost in a linear fashion along the microtubules. Enlarging the PLA image shows that each dot is very small - just a few pixels - please provide additional explanation including the minimal detection limit for the method, and why the images differ. If the standard immunofluorescence signal was enhanced, for example with the use of two secondaries, what is observed? Is the distribution of HMMR similar for both dendrites and axons? Microtubule polarity differs in these locations, so greater attention to this point seems of interest. There is a significant amount of punctate HMMR in the cytoplasm (or outside the cytoplasm?) in Figure S5; this is concerning. Please outline the cell edge for ease of visualization. What is the distribution of HMMR in a cell that has been treated with cold and/or nocodazole to disassemble the microtubules? is the signal lost?

The reasons images of the endogenous HMMR (Figure S3) and the PLA with tubulin and HMMR antibodies (Figure 2C) differ are due to the following reasons. o PLA utilizes two primary antibodies to target two different epitopes on HMMR and βIII-tubulin. It is conceivable that not every anti-HMMR antibody has the correct orientation and/or proximity (<40 nm) toward the anti-β-III-tubulin antibody to enable DNA amplification. This results in the shortage of PLA puncta compared to immunofluorescence signals.

• The creator of PLA has pointed out that in situ PLA is a method based upon equilibrium reactions and several enzymatic steps. Therefore, only a fraction of the inter-acting molecules is detected (Weibrecht et al., 2010).

We have not used signal enhancing immunofluorescence staining methods [e.g., using tertiary antibodies or tyramide signal amplification (TSA)] to detect HMMR. This is mainly because HMMR signal is strong enough to be detected using standard immunofluorescence staining.

Regarding the question “Is the distribution of HMMR similar for both dendrites and axons?” The reviewer raised a very important issue about the polarity difference of microtubules in axons (uniform) and dendrites (mixed). We were aware of such issue and very carefully examined the distribution and signal intensity of HMMR in axons vs dendrites. However, no differences were detected.

The reviewer mentioned that “there is a significant amount of punctate HMMR in the cytoplasm (or outside the cytoplasm?) in Figure S5; this is concerning. Please outline the cell edge for ease of visualization.” Instead of outlining the cell edge, we have selected another image to facilitate the visualization of HMMR signals. There are indeed HMMR signals outside the cell. However, these outside signals are usually weaker and smaller in size compared to those inside the cell.

After the examination of neurons expressing AcGFP-mHMMR with or without 100 nM nocodazole treatment, we did not notice any difference of AcGFP-mHMMR in distribution. We did not examine the distribution and signal intensity of the endogenous HMMR.

(7) To determine if HMMR alters microtubule stability, the authors examine the distribution of acetylated tubulin and resistance to nocodazole-induced microtubule disassembly. In Figure 3 please show immunofluorescence images of the acetylated tubulin staining, not just the ratio images; the color is not obviously different in the various panels shown. For statistical analysis, see the comment above for Figure 1. For the nocodazole experiment, a similar change in neurite length following drug treatment was observed (Figure 3H), for the experimental and control, even though the starting length was greater in the overexpressing cells. Please consider the possibility that in both cases the microtubules are only partially resistant to nocodazole and that HMMR is not changing the fraction of microtubules that are sensitive to the drug. The cells were treated at 3 DIV; the authors note that more stable microtubules accumulate with time; how does time in culture impact stability? Often, acute treatment with a high concentration of nocodazole is used to assay microtubule stability; here the authors used a low (nM) concentration for 2 days (chronic). Why not use a higher concentration (1-10 μM) for a shorter incubation? The data show that overexpression of HMMR results in curved, buckled microtubules are these microtubules more acetylated and/or retained after nocodazole treatment?

The reviewer suggested that we show immunofluorescence images of the acetylated tubulin staining, not just the ratio images. But we still believe showing the ratio images is the better approach. This is because the microtubules density can be different from neuron to neuron. Showing acetylated tubulin may provide a false impression when the overall microtubule density is higher or lower in a particular neuron. We realized that “16 colors” pseudo-color scheme has the cyan color at the lower intensity which can sometimes be confused with the white color at the higher intensity. Therefore, we changed the pseudocolor from “16 colors” to “fire” for Figure 3B and 3E to better visualize these images so that they appear more consistent with the quantitative data.

The reviewer raised a very good question regarding the possibility that HMMR is not changing the fraction of microtubules that are sensitive to nocodazole. We re-conducted the same experiment and used a series of different nocodazole concentrations. While the addition of nocodazole causes a concentration-dependent reduction of total neurite length in both AcGFP and AcGFP-mHMMR expressing neurons, there are subtle differences in the susceptibility of neurite length to the concentration of nocodazole. 1) 10 nM nocodazole treatment causes a significant reduction of neurite length in AcGFP expressing neurons, but not in AcGFP-mHMMR expressing neurons. This result indicates that AcGFP-mHMMR expression increases the tolerance of neurite elongation toward 10 nM nocodazole treatment. 2) 50 nM and 100 nM nocodazole treatment exhibits no statistical significance in AcGFP expressing neurons, suggesting that 50 nM nocodazole has reached maximal effectiveness. In AcGFP-mHMMR expressing neurons, 100 nM nocodazole further reduces the neurite length compared to the 50 nM group. These results argue against the possibility that HMMR does not change the fraction of microtubules that are sensitive to nocodazole. We have revised Figure 3H accordingly.

The reviewer asked why we did not use the acute nocodazole treatment (μM concentration) to assess the effect of Hmmr on microtubule stability. This is because we used the neurite length as an indicator for microtubule stability. That is why the chronic treatment was chosen to produce a more detectable effect on neurite length.

The reviewer asked whether the looped microtubules caused by HMMR overexpression are more acetylated and/or nocodazole resistant. While we do not have direct evidence to answer the reviewer’s question, we can deduce the answer from our observations. We noticed that looped microtubules are only present when HMMR is highly expressed (i.e., using lipofection to introduce HMMR-expressing plasmid) but not when HMMR is mildly expressed (i.e., using electroporation to introduce HMMR-expressing plasmid). From these observations, we can conclude that HMMR is more abundantly present on looped microtubules. Since HMMR overexpression leads to higher microtubule acetylation (Figure 3E), looped microtubules which contains more HMMR are most likely to be more acetylated.

(8) An additional measure of microtubule dynamics is to measure the growth of microtubules using a live cell marker for microtubule plus ends. Such experiments were performed, using tagged EB3. The images are rather fuzzy. Parameters of microtubule dynamics were measured at three locations - is there data that the authors can cite about any differences in dynamics in control cells at these locations? They look very similar, so it is not clear why the different locations were used. It is not possible to learn much from the kymographs which look similar for all panels; I would remove these unless they can be changed or labeled to help the reader. Data is presented for three shRNA reagents. No data are presented to document the extent to which the protein is depleted with these reagents. This should be fixed. Alternatively, an RNAi pool could be utilized. Is there a control for off-target effects? For the analysis were all the comets used to generate the average values? What about a comparison of the average of each trial - not each comet?

In our previous publication (Chen et al., 2017), it was discovered that a significant reduction of EB3 emanation frequency can be detected at the tip and the base of the neurite but not in the middle of the neurite in TPX2-depleted neurons. The reason for this difference is due to the presence of RanGTP at the tip and the base of the neurite. Since RanGTP has also been shown to regulate the interaction between HMMR and TPX2 in the cell-free system (Scrofani et al., 2015), it is possible that the same phenomenon can be observed in HMMR-depleted neurons. This is why we examined those 3 ROIs in Figure 4.

We notice that photobleaching causes the EB3-mCherry signal to diminish at later time points, which made it difficult to observe the differences amongst kymographs. In the revised Figure 4B and 4D, we removed the second half of all the kymographs to make the differences more obvious.

The reviewer mentioned that there are no data documenting the extent to which the protein is depleted with the shRNAs. These data are shown in Figure S2, in which we quantified the HMMR protein level in the soma and along the neurite in neurons expressing different shRNA molecules.

The reviewer asked whether there is a control for off-target effects. The answer is yes. We performed the rescue experiment to control for off-target effects, which is shown in Figure S1.

We revised Figure 4 so that the dynamic properties of EB3 are quantified using the average of each experimental repetition.

(9) In a final experiment, the authors examine the distribution of TPX2, a binding partner of HMMR. Include a standard immunofluorescence in addition to PLA to illustrate the distribution of TPX2. The quantification used was the inter puncta distance; please quantify the signal in control and treated cells.

The reviewer asked us to include a standard immunofluorescence staining to illustrate the distribution of TPX2. We have done that in our previous publication (Chen et al., 2017) and TPX2 localizes primarily to the centrosome (https://www.nature.com/articles/srep42297/figures/2). In order to enhance the weak signal of TPX2 along the neurite, we actually needed to use PLA in that publication (https://www.nature.com/articles/srep42297/figures/3).

Proximity ligation assay (PLA) generates fluorescent signals based on a local enzymatic reaction which catalyzes the amplification of a specific DNA sequence that can then be detected using a red fluorescent probe. Because this enzymatic reaction is not linear, the amount of amplified DNA nor the intensity of the fluorescence does not correlate with the strength of the interaction (Soderberg et al., 2006). As a result, quantification of PLA is typically done by counting the number of fluorescent puncta per unit area or by calculating the area containing fluorescent signal (not signal intensity) per unit area in the case that PLA signals are too strong and coalesced. That is why our quantification is based on the distance between PLA fluorescent puncta, not the fluorescent signal intensity.

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Author response:

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

Reviewer #1 (Public Review):

Summary:

The authors set up a pipeline for automated high-throughput single-molecule fluorescence imaging (htSMT) in living cells and analysis of molecular dynamics

Strengths:

htSMT reveals information on the diffusion and bound fraction of molecules, dose-response curves, relative estimates of binding rates, and temporal changes of parameters. It enables the screening of thousands of compounds in a reasonable time and proves to be more sensitive and faster than classical cell-growth assays. If the function of a compound is coupled to the mobility of the protein of interest, or affects an interaction partner, which modulates the mobility of the protein of interest, htSMT allows identifying the modulator and getting the first indication of the mechanism of action or interaction networks, which can be a starting point for more in-depth analysis.

Weaknesses:

While elegantly showcasing the power of high-throughput measurements, the authors disclose little information on their microscope setup and analysis procedures. Thus, reproduction by other scientists is limited. Moreover, a critical discussion about the limits of the approach in determining dynamic parameters, the mechanism of action of compounds, and network reconstruction for the protein of interest is missing. In addition, automated imaging and analysis procedures require implementing sensitive measures to assure data and analysis quality, but a description of such measures is missing.

The reviewer rightly highlights both the power and complexity in high throughput assay systems, and as such the authors have spent significant effort in first developing quality control checks to support screening. We discuss some of these as part of the description and characterization of the platform. We added additional details into the manuscript to help clarify. The implementation of our workflow for image acquisition, processing and analysis relies heavily on the specifics of our lab hardware and software infrastructure. We have added additional details to the text, particularly in the Methods section, and believe we have added enough information that our results can be reproduced using the suite of tools that already exist for single molecule tracking.

The reviewer also points out that all assays have limitations, and these have not been clearly identified as part of our discussion of the htSMT platform. We have also added some comments on the limitations of the current system and our approach.

Reviewer #2 (Public Review):

Summary:

McSwiggen et al present a high throughput platform for SPT that allows them to identify pharmaceutics interactions with the diffusional behavior of receptors and in turn to identify potent new ligands and cellular mechanisms. The manuscript is well written, it provides a solid new mentor and a proper experimental foundation

Strengths:

The method capitalizes and extends to existing high throughput toolboxes and is directly applied to multiple receptors and ligands. The outcomes are important and relevant for society. 10^6 cells and >400 ligands per is a significant achievement.

The method can detect functionally relevant changes in transcription factor dynamics and accurately differentiate the ligand/target specificity directly within the cellular environment. This will be instrumental in screening libraries of compounds to identify starting points for the development of new therapeutics. Identifying hitherto unknown networks of biochemical signaling pathways will propel the field of single-particle live cell and quantitative microscopy in the area of diagnostics. The manuscript is well-written and clearly conveys its message.

Weaknesses:

There are a few elements, that if rectified would improve the claims of the manuscript.

The authors claim that they measure receptor dynamics. In essence, their readout is a variation in diffusional behavior that correlates to ligand binding. While ligand binding can result in altered dynamics or /and shift in conformational equilibrium, SPT is not recording directly protein structural dynamics, but their effect on diffusion. They should correct and elaborate on this.

This is an excellent clarifying question, and we have tried to make it more explicit in the text. The reviewer is absolutely correct; we’re not using SPT to directly measure protein structural dynamics, but rather the interactions a given protein makes with other macromolecules within the cell. So when an SHR binds to ligand it adopts conformations that promote association with DNA and other protein-protein interactions relevant to transcription. This is distinct from assays that directly measure conformational changes of the protein.

L 148 What do the authors mean 'No correlation between diffusion and monomeric protein size was observed, highlighting the differences between cellular protein dynamics versus purified systems'. This is not justified by data here or literature reference. How do the authors know these are individual molecules? Intensity distributions or single bleaching steps should be presented.

The point we were trying to make is that the relative molecular weights for the monomer protein (138 kDa for Halo-AR, 102 kDa for ER-Halo, 122 kDa for Halo-GR, and 135 kDa for Halo-PR) is uncorrelated with its apparent free diffusion coefficient. Were we to make this measurement on purified protein in buffer, where diffusion is well described by the Stokes Einstein equation, one would expect to see monomer size and diffusion related. We’ve clarified this point in the manuscript.

Along the same lines, the data in Figs 2 and 4 show that not only the immobile fraction is increased but also that the diffusion coefficient of the fast-moving (attributed to free) is reduced. The authors mention this and show an extended Fig 5 but do not provide an explanation.

This is an area where there is still more work to do in understanding the estrogen receptor and other SHRs. As the reviewer says, we see not only an increase in chromatin binding but also a decrease in the diffusion coefficient of the “free” population. A potential explanation is that this is a greater prevalence of freely-diffusing homodimers of the receptor, or other protein-protein interactions (14-3-3, P300, CBP, etc) that can occur after ligand binding. Nothing in our bioactive compound screen shed light on this in particular, and so we can only speculate and have refrained from drawing further conclusions in the text.

How do potential transient ligand binding and the time-dependent heterogeneity in motion (see comment above) contribute to this? Also, in line 216 the authors write "with no evidence" of transient diffusive states. How do they define transient diffusive states? While there are toolboxes to directly extract the existence and abundance of these either by HMM analysis or temporal segmentation, the authors do not discuss or use them.

Throughout the analysis in this work, we consider all of tracks with a 2-second FOV as representative of a single underlying population and have not looked at changes in dynamics within a single movie. As we show in the supplemental figures we added (see Figure 3, figure supplement 1), this appears to be a reasonable assumption, at least in the cases we’ve encountered in this manuscript. For experiments involving changes in dynamics over time, these are experiments where we’ve added compound simultaneous with imaging and collect many 2-second FOVs in sequence to monitor changes in ER dynamics. In this case when we refer to “transient states,” we are pointing out that we don’t observe any new states in the State Array diagram that exist in early time points but disappear at later time point.

The reviewer suggests track-level analysis methods like hidden Markov models or variational Bayesian approaches which have been used previously in the single molecule community. These are very powerful techniques, provided the trajectories are long (typically 100s of frames). In the case of molecules that diffuse quickly and can diffuse out of the focal plane, we don’t have the luxury of such long trajectories. This was demonstrated previously (Hansen et al 2017, Heckert el al 2022) and so we’ve adopted the State Array approach to inferring state occupations from short trajectories. As the reviewer rightly points out, this approach potentially loses information about state transitions or changes over time, but as of now we are not aware of any robust methods that work on short trajectories.

The authors discuss the methods for extracting kinetic information of ligand binding by diffusion. They should consider the temporal segmentation of heterogenous diffusion. There are numerous methods published in journals or BioRxiv based on analytical or deep learning tools to perform temporal segmentation. This could elevate their analysis of Kon and Koff.

We’re aware of a number of approaches for analyzing both high framerate SMT as well as long exposure residence time imaging. As we say above, we’re not aware of any methods that have been demonstrated to work robustly on short trajectories aside from the approaches we’ve taken. Similarly, for residence time imaging there are published approaches, but we’re not aware of any that would offer new insight into the experiments in this study. If the reviewer has specific suggestions for analytical approaches that we’re not aware of we would happily consider them.

Reviewer #3 (Public Review):

Summary:

The authors aim to demonstrate the effectiveness of their developed methodology, which utilizes super-resolution microscopy and single-molecule tracking in live cells on a high-throughput scale. Their study focuses on measuring the diffusion state of a molecule target, the estrogen receptor, in both ligand-bound and unbound forms in live cells. By showcasing the ability to screen 5067 compounds and measure the diffusive state of the estrogen receptor for each compound in live cells, they illustrate the capability and power of their methodology.

Strengths:

Readers are well introduced to the principles in the initial stages of the manuscript with highly convincing video examples. The methods and metrics used (fbound) are robust. The authors demonstrate high reproducibility of their screening method (R2=0.92). They also showcase the great sensitivity of their method in predicting the proliferation/viability state of cells (R2=0.84). The outcome of the screen is sound, with multiple compounds clustering identified in line with known estrogen receptor biology.

Weaknesses:

• Potential overstatement on the relationship of low diffusion state of ER bound to compound and chromatin state without any work on chromatin level.

We appreciate the reviewers caution in over-interpreting the relationship between an increase in the slowest diffusing states that we observe by SMT and bona fide engagement with chromatin. In the case of the estrogen receptor there is strong precedent in the literature showing increases in chromatin binding and chromatin accessibility (as measured by ChIP-seq and ATAC-seq) upon treatment with either estradiol or SERM/Ds. Taken together with the RNA-seq, we felt it reasonable to assume all the trajectories with a diffusion coefficient less that 0.1 µm2/sec were chromatin bound.

• Could the authors clarify if the identified lead compound effects are novel at any level?

Most of the compounds we characterize in the manuscript have not previously been tested in an SMT assay, but many are known to functionally impact the ER or other SHRs based on other biochemical and functional assays. We have not described here any completely novel ER-interacting compounds, but to our knowledge this is the first systematic investigation of a protein showing that both direct and indirect perturbation can be inferred by observing the protein’s motion. Especially for the HSP90 inhibitors, the observation that inhibiting this complex would so dramatically increase ER chromatin-binding as opposed to increasing the speed of the free population is counterintuitive and novel.

• More video example cases on the final lead compounds identified would be a good addition to the current data package.

Reviewer #1 (Recommendations For The Authors):

General:

• More information on the microscope setup and analysis procedures should be given. Since custom code is used for automated image registration, spot detection, tracking, and analysis of dynamics, this code should be made publicly available.

Results:

• line 97: more details about the robotic system and automatic imaging, imaging modalities, and data analysis procedures should be given directly in the text.

Additional information added to text and methods

• line 100: we generated three U2OS cell lines --> how?

Additional information added to text and methods

• line 101: ectopically expressing HaloTag fused proteins --> how much overexpression did cells show?

The L30 promoter tends to produce fairly low expression levels. The same approach was used for all ectopic expression plasmids, and for the SHRs the expression levels were all comparable to endogenous levels. We have not checked this for H2B, Caax and free Halo but given that the necessary dye concentration to achieve similar spot densities is within a 10-fold range for all constructs, its reasonable to say that those clonal cell lines will also have modest Halotag expression.

• line 107: Single-molecule trajectories measured in these cell lines yielded the expected diffusion coefficients --> how was data analysis performed?

Additional information added to text and methods

• line 109: how was the localization error determined?

Additional information added to text and methods

• line 155: define occupation-weighted average diffusion coefficient.

Additional information added to text and methods

• line 157: with 34% bound in basal conditions and 87% bound after estradiol treatment  contradicts figure 2b, where the bound fraction is up to 50% after estradiol treatment.

Line 157 is the absolute fraction bound, figure 2b is change in fbound

• line 205: Figure 2c is missing.

Fixed

• line 215: within minutes --> how was this data set obtained? which time bins were taken?

Additional information added to text and methods

• line 216: with no evidence of transient diffusive states  What is meant by transient diffusive state? It seems all time points have a diffusive component, which decreases over time.

Additional information added to text and methods

The diffusive peak decreases, the bound peak increases but no other peaks emerge during that time (e.g. neither super fast nor super slow)

• line 225: it seems that fbound of GDC-0810 and GDC-0927 are rather similar in FRAP experiments, please comment, how was FRAP done?

FRAP is in the methods section. The curves and recovery times are quite distinct, is the reviewer looking at

• line 285: reproducibly: how often was this repeated?

Information added to the manuscript

• line 285: it would be necessary to name all of the compounds that were tested, e.g. with an ID number in the graph and a table. This also refers to extended data 7 and 8.

Additional supplemental file with the list of bioactive compounds tested will be included.

• line 290/1: what is meant by vendor-provided annotation was poorly defined?

Additional information added to text and methods. Specifically, the “other” category is the most common category, and it includes both compounds with unknown targets/functions as well as compound where the target and pathway are reasonably well documented. Hence, we applied our own analysis to better understand the list of active compounds.

Figures:

• fig. 2-6: detailed statistics are missing (number of measured cells, repetitions, etc.).

We have added clarifying information, including an “experiment design and sample size” section in the Methods.

• fig. 3: the authors need to give a list with details about the 5067 compounds tested,

Additional supplemental file with the list of bioactive compounds tested will be included.

• extended data 1c: time axis does not correspond to the 1.5s of imaging in the text, results line 127.

Axes fixed

• extended data 3: panel c and d are mislabeled.

Panel labels fixed

Methods:

• line 746: HILO microscope: the authors need to explain how they can get such large fields of view using HILO

Additional details added to the materials and methods. The combination of the power of the lasers, the size of the incident beam out of the fiber optic coupling device and the sCMOS camera are the biggest components that enable detection over a larger field of view.

• line 761: it is common practice to publish the analysis code. Since the authors wrote their own code, they should publish it

Our software contains proprietary information that we cannot yet release publicly. Comparable results can be achieved with HILO data using publicly-available tools like utrack. State Arrays code is distributed and the parameters used are listed in the M&M.

Reviewer #2 (Recommendations For The Authors):

The writing and presentation are coherent, concise, and easy to follow.

The authors should consider justifying the following:

Why is 1.5s imaging time selected? Topological and ligand variations may last significantly longer than this. The authors should present at least for one condition the same effect images for longer.

Related to the similar comment above, we added a figure examining the jump length distribution as a function of frame. Over the 6 seconds of data collection the jump length distribution is unchanged, suggesting it is reasonable to consider all the trajectories within an FOV as representative of the same underlying dynamical states.

The authors miss the k test or T test in their graphs.

We chose to apply the Kurskal-Wallis test in the context of the bioactive screen to assess whether a grouping of compounds based on their presumed cellular target was significantly different from the control even when individual compounds might not by themselves raise to significance. In this case many of the pathway inhibitors are subtle and not necessarily obvious in their difference. In the other cases throughout the manuscript, whether two conditions are statistically distinguishable is rarely in question and of far less importance to the conclusions in the manuscript than the magnitude of the difference. We’ve added statistical tests where appropriate.

The overall integrated area of Fig 4a appears to reduce upon ligand addition. Data appear normalized but the authors should also add N (number of molecules) on top of the graphs.

While the integrated area may appear to decrease, all State Array analysis is performed by first randomly sampling 10,000 trajectories from the assay well and inferring state distribution on those 10,000. This has been clarified in the figure legend and in the Methods.

Minor

Extended Figure 3 legend c, d appear swapped and incorrectly named in the text.

Panel labels fixed

L 197 but this appears not to BE a general feature of SHRs (maybe missing Be).

Error fixed

L205 authors refer to Figure 2c, which does not exist.

Panel reference fixed

Reviewer #3 (Recommendations For The Authors):

Among minor issues:

In Figure 1B, if the authors could specify how they discriminate the specific cell lines from the mixed context, it would enhance clarity. Could they perform additional immunofluorescence to understand how the assignment is determined? Alternatively, could they also show the case with isolated cell lines in an unmixed context?

Immunofluorescence would be a challenge given that there is not a good epitope to distinguish the three ectopically-expressed genes from each other or from endogenous proteins in the case of H2B and CaaX. We are really reliant on the single cell dynamics to determine the likely cell identity. That said, we’ve added graphs of a number of individual cell State Arrays from the same data graphed in 1A which support the notion that it’s reasonable to assume a cells identity given the observed dynamics.

In Extended Figure 2F: possibly a CHip-Seq experiment would be more directly qualified to state the effect of ER ligand on ER ability to bind chromatin.

This is true. Presumably ER that is competent at activating transcription of ER-responsive genes is also capable of binding DNA. ChIP would be the more direct measure, but would not address whether the protein was functional. We chose to balance these measuring these two aspects of ER biology by pairing dynamics with the end-point transcription readout.

In Figure 3: A representation with plate-by-plate orientation along the x-axis, with controls included in each plate, would be more appropriate to reflect the consistency of the controls used in the assay across different plates. Currently, all controls are pooled in one location, and we cannot appreciate how the controls vary from plate to plate.

Figure added to the supplement

Also in this figure, a general workflow of the screen down to segmentation/analysis would be a great add-on.

New figure added to the supplement and reflected in the textual description of the platform

In Extended Figures 3B and C an add-on of the positive and negative control would make the figure more convincing.

Addressed as part of figure added to the supplement

Is there any description of compound leads identified that is novel in nature in relation to impact on ER, and if so could it be stated more clearly in the text as novel finding?

To our knowledge, the impact of HSP inhibition in increasing ER-chromatin association has never been described, neither has the link between inhibition post-translation modifying enzymes like the CDKs or mTOR and ER dynamics ever been described. We added clarifying text to the manuscript