Author Response

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

Re: Revised author response for eLife-RP-RA-2023-90135 (“The white-footed deermouse, an infection-tolerant reservoir for several zoonotic agents, tempers interferon responses to endotoxin in comparison to the mouse and rat” by Milovic, Duong, and Barbour”)

The revised manuscript has taken into account all the comments and questions of the two reviewers. Our responses to each of the comments are detailed below. In brief, the modifications or additional materials for the revision each specifically address a reviewer comment. These modifcations or materials include the following….

• a more in-depth consideration of sample sizes

• a better explanation of what p values signify for a GO term analysis

• a more detailed account of the selection of the normalization procedure for cross-species targeted RNA-seq (including a new supplemental figure)

• several more box plots in supplementary materials to complement the scatterplots and linear regressions of the figures of the primary text

• provision in a public access repository of the complete data for the RNA-seq analyses as well as primary data for figures and tables as new supplementary tables

• the expansion of description of the analysis done for the revision of Borrelia hermsii infection of P. leucopus. This included a new table (Table 10 of the revision) • development of the possible relevance of finding for longevity studies by citing similarities of the findings in P. leucopus with those in the naked mole-rat

• what we think is a better assessment of differences between female and male P. leucopus for this particular study, while still keeping focus on DEGs in common for females and males. This included a new figure (Figure 4 of the revision).

• removal of reference to a “inverse” relationship between Nos2 and Arg1 while still retaining ratios of informative value

We note that in the interval between uploading the original bioRxiv preprint and now we learned of the paper of Gozashti, Feschotte, and Hoekstra (reference 32), which supports our conception of the important place of endogenous retroviruses in the biology and ecology of deermice. This is the only addition or modification that was not a direct response to a reviewer comment or question, but it was germane to one of Reviewer #1’s comments (“Regarding..”).

Reviewer #1:

Supplemental Table 1 only lists genes that passed the authors statistical thresholds. The full list of genes detected in their analysis should be included with read counts, statistics, etc. as supplemental information.

We agree that provision of the entire lists of reference transcripts and the RNA-seq results for each of the 40 animals is merited. These datasets are too large for what the journal’s supplementary materials resource was intended for, so we have deposited them at the Dryad public access repository.

While P. leucopus is a critical reservoir for B. burgdorferi, caution should be taken in directly connecting the data presented here and the Lyme disease spirochete. While it's possible that P. leucopus have a universal mechanism for limiting inflammation in response to PAMPs, B. burgdorferi lack LPS and so it is also possible the mechanisms that enable LPS tolerance and B. burgdorferi tolerance may be highly divergent.

The impetus for the study was the phenomenon of tolerance of infection of P. leucopus by a number of different kinds of pathogens, not just B. burgdorferi. We take the reviewer’s point, though. Certainly, the white-footed deermouse is probably most notable at-large for its role as a reservoir for the Lyme disease agent. We doubt that the species responses to LPS and to the principal agonists of B. burgdorferi are “highly divergent”, though. Other than the TLR itself-TLR4 for LPS vs the heterodimer TLR2/TLR1 for the lipoproteins of these spirochetes--the downstream signaling is generally similar for amounts comparable in their agonist potency.

We had thought that we had addressed this distinction for B. burgdorferi and other Borreliaceae members by referring to the earlier study. But we agree with the reviewer that what was provided on this point was insufficient in the context of the present work. Accordingly, for the revision we have added a new analysis of the data on experimental infection of P. leucopus with Borrelia hermsii, which lacks LPS and for which the TLR agonists eliciting inflammation are lipoproteins. We do this in a format (new Table 6) that aids comparison with the LPS experimental data elsewhere in the article. As the manuscript references, B. burgdorferi infection of P. leucopus elicits comparatively little inflammation in blood even at the height of infection. While this phenomenon with the Lyme disease agent was part of the rationale driving these studies, the better comparison with LPS was 5 days into B. hermsii infection when the animals are spirochetemic.

Statistical significance is binary and p-values should not be used as the primary comparator of groups (e.g. once a p-value crosses the deigned threshold for significance, the magnitude of that p-value no longer provides biological information). For instance, in comparing GO-terms, the reason for using of high p-value cutoffs ("None of these were up-regulated gene GO terms with p values < 1011 for M. musculus.") to compare species is unclear. If the authors wish to compare effect sizes, comparing enrichment between terms that pass a cutoff would likely be the better choice. Similarly, comparing DEG expression by p-value cutoff and effect size is more meaningful than analyses based on exclusively on p-value: "Of the top 100 DEGs for each species by ascending FDR p value." Description in later figures (e.g. Figure 4) is favored.

Effect sizes--in this case, fold-changes--were taken into account for GO term analysis and were specified in the settings that are described. So, any gene that was “counted” for consideration for a particular GO term would have passed that threshold and with a falsediscovery corrected p value of a specified minimum. There is no further scoring of the “hit” based upon the magnitude of the p value beyond that point. It is, as the reviewer writes, binary at that point. We are in agreement on those principles.

As we understand the comment above, though, the p-values referred to are in regard to the GO term analysis itself. The objective was discovery followed by inference. The situation was more like a genome-wide association study (GWAS) study. This is not strictly speaking a hypothesis test, because there was no stated hypothesis ahead of time or one driving the design. The “p value” for something like GO term analysis or GWAS provides an estimate of the strength of the association. It is not binary in that sense. The lower the p value, the greater confidence about the association. In a GWAS of a human population an association of a trait with a particular SNP or indel is usually not taken seriously unless the p value is less than 10^-7 or 10^-8. In the case of GO terms, the p value approximates (but is not equivalent to) the number of genes that are differentially expressed that belong to a GO cluster out of the total number of genes that define that cluster. The higher the proportion of the genes in the cluster that are associated with a treatment (LPS vs. saline), the lower the p value. Thus, it provides information beyond the point at which it would be rightly deemed of little additional value in many hypothesis testing circumstances.

That said, we agree that the original manuscript could have been clearer on this point and have for the revision expanded the description of the GO term analysis in the Methods, including some explanation for a reader on what the p value signifies here. We also refrain from specifying a certain p value for special attention and merely list 20 by ascending p value.

The ability to use of CD45 to normalize data is unclear. Authors should elaborate both on the use of the method and provide some data how the data change when they are normalized. For instance, do correlations between untreated Mus and Peromyscus gene expression improve? The authors seem to imply this should be a standard for interspecies comparison and so it would be helpful to either provide data to support that or, if applicable, use of the technique in literature should be referenced.

The reviewer brings up an important point that we considered addressing in more depth for the original manuscript but in the end deferred to considerations about length and left it out.

But we are glad to address this here, as well as in the revised manuscript.

We did not intend to imply either that this particular normalization approach had been done before by others or that it “should” be a standard. We are not aware of another report on this, and it would be up to others whether it would be useful or not for them. We made no claim about its utility in another model or circumstance. The challenge before us was to do a comparative analysis of transcription in the blood not just for animals of one species under different conditions but animals of two different genera under different conditions. A notable difference between the animals was in their white blood cell counts, as this study documents. White cells would be the source of a majority of transcripts of potential relevance here, but there would also be mRNA for globins, from reticulocytes, from megakaryocytes, and likely cell-free RNA with origins in various tissues. If the white cell numbers differed, but the non-white cell sources of RNA did not, then there could be unacknowledged biases.

It would be like comparing two different kinds of tissues and assuming them to be the same in the types and numbers of cells they contained. Four hours after a dose of LPS the liver cells (or brain cells) would differ in their transcriptional profiles from untreated the livers (or brains) of untreated animals for sure, but there would not be much if any change in the numbers of different kinds of cells in the liver (or brain) within 4 hours. The blood can change a lot in composition within that time frame under these same conditions. Some sort of accounting for differing white cell numbers in the blood in different outbred animals of two species seemed to be called for.

The normalization that was done for the genome-wide analysis was not based on a particular transcript, but instead was based on the total number of reads, the lengths of the reference transcripts, and the distributions of reads matching to the tens of thousands of references for each sample. This was done according to what are standard procedures by now for bulk RNAseq analyses. Because the reference transcript sets for P. leucopus and M. musculus differed in their numbers and completeness of annotation, we did not attempt any cross-species comparison for the same set of genes at that point. That would not be possible because they were not entirely commensurate.

The GO term analysis of those results provided the leads for the more targeted approach, which was roughly analogous to RT-qPCR. For a targeted assay of this sort, it is common to have a “housekeeping gene” or some other presumably stably transcribed gene for normalization. A commonly used one is Gapdh, but we had previously found that Gapdh was a DEG itself in the blood in P. leucopus and M. musculus at the four hour mark after LPS. The aim was to provide for some adjustment so datasets for blood samples differing in white blood cell counts could be compared. Two options were the 12S ribosomal RNA of the mitochondria, which would be in white cells but not mature erythrocytes, and CD45, which has served an approximately similar function for flow cytometry of the blood. As described in what has been added for the revision and the supplementary materials, we compared these different approaches to normalization. Ptprc and 12S rRNA were effectively interchangeable as the denominator with identifying DEGs of P. leucopus and M. musculus and cross-species comparisons.

Regarding the ISG data-is a possible conclusion not that Peromyscus don't upregulate the antiviral response because it's already so high in untreated rodents? It seems untreated Peromyscus have ISG expression roughly equivalent to the LPS mice for some of the genes. This could be compared more clearly if genes were displayed as bar plots/box and whisker plots rather than in scatter plots. It is unclear why the linear regression is the key point here rather than normalized differences in expression.

In answer to the question: yes, that is possible. In the interval between uploading of the manuscript and this revision, we became aware of a study by Gozashti and Hoekstra published this year in Molecular Biology and Evolution (reference 32) and reporting on the “massive invasion” of endogenous retroviruses in P. maniculatus and the defenses deployed in response to achieve silencing. We cite this work and discuss it, including related findings for P. leucopus, in the revision.

We had originally intended to include box plots as well as scatterplots with regressions for the data, but thought it would be too much and possibly considered redundant. But with this encouragement from the reviewer we provide additional box plots in supplementary materials for the revision.

Some sections of the discussion are under supported:

The claim that low inflammation contributes to increased lifespan is stated both in the introduction and discussion. Is there justification to support this? Do aged pathogen-free mice show more inflammation than aged Peromyscus?

We respectively point out that there was not a claim of this sort. We stated a fact about P. leucopus’ longevity. We made no statement connecting longevity and inflammation beyond the suggestion in the introduction that the explanation(s) for infection tolerance might have some bearing for studies on determinants of life span.

But the reviewer’s comment prompted further consideration of this aspect of Peromyscus biology. This led eventually to the literature on the naked mole-rat, which seems to be the rodent with the longest known life span and the subject of considerable study. The discussion section of the revision has an added paragraph on some of the similarities of P. leucopus and the naked mole-rat in terms of neutrophils, expression of nitric oxide synthase 2 in response to LPS, and type 1 interferon responses. While this is far from decisive, it does serve to connect some of the dots and, hopefully, is considered at least partially responsive to the reviewer’s question.

The claim that reduced Peromyscus responsiveness could lead to increased susceptibility to infection is prominently proposed but not supported by any of the literature cited.

There was not this claim. In fact, it was framed as a question, not a statement. Nevertheless, we think we understand what the comment is getting at and acknowledge in the revision that there may be unexamined circumstances in which P. leucopus may be more vulnerable.

References to B. burgdorferi, which do not have LPS, in the discussion need to ensure that the reader understands this and the potential that responses could be very different.

We think we addressed this comment in a response above.

Reviewer #2:

1. How were the number of animals for each experiment selected? Was a power analysis conducted?

A power analysis of any meaning for bulk RNA-seq with tens of thousands of reference transcripts, each with their own variance, and a comparison of animals of two different genera is not straight forward. Furthermore, a specific hypothesis was not being tested. This was a broad, forward screen. But the question about sample sizes is one that deserves more attention than the original manuscript provided. This now provided in added text in two places in Methods ( “RNA-seq” and “Genome-wide different gene expression”) in the revision.

1. The authors conducted a cursory evaluation of sex differences of P. leucopus and reported no difference in response except for Il6 and Il10 expression being higher in the males than the females in the exposed group. The data was not presented in the manuscript. Nor was sex considered for the other two species. A further discussion of the role that sex could play and future studies would be appreciated.

We agree that the limited analysis of sex differences and the undocumented remark about Il6 and Il10 expression in females and males warranted correction. For the revision we removed that analysis of targeted RNA-seq of P. leucopus from the two different studies. For this study we were looking for differences that applied to both species. This was the reason that there were equal numbers of females and males in the samples. We agree that further investigation of differences between sexes in their responses is of interest but is probably best left for “future studies”.

But in revision we do not entirely ignore the question of sex of the animal and provide an additional analysis of the bulk RNA-seq for P. leucopus with regard to differences between females and males. This basically demonstarted an overall commensurability between sexes, at least for the purposes of the GO term analysis and subsequent targeted RNA-seq, but did reveal some exceptions that are candidate genes for those future studies.

In the revision, we also add for the discussion and its “study limitations” section a disclaimer about possibly missing sex associated differences because the groups were mixed sexes.

1. The ratio of Nos2 and Arg1 copies for LPS treated and control P. leucopus and M.musculus in Table 3 show that in P. leucopus there is not a significant difference but in M.musculus there is an increase in Nos2 copies with LPS treatment. The authors then used a targeted RNA-seq analysis to show that in P. leucopus the number of Arg1 reads after LPS treatment is significantly higher than the controls. These results are over oversimplified in the text as an inverse relationship for Nos2/Arg1 in the two species.

We agree. In addition to providing box plots for Arg1 and Nos2, as suggested by Reviewer #1, we also replaced “ratio” in commenting on Arg1 and Nos2, with “differences in Nos2 and Arg1 expresssion” replacing “ratio of Nos2 to Arg1 expression” at one place. At another place we have removed “inverse” with regard to Nos2 and Arg1. But we respectfully decline to remove Nos2/Arg1 from Figure 5 (now Figure 6) or inclusion of Nos2/Arg1 ratios elsewhere. According to our understanding there need not be an inverse relationship for a ratio to have informative value.

Recommendations For the Authors

We thank the two reviewers for their constructive recommendations and suggestions, in some case pointing out errors we totally missed. For the great majority, the recommendations were followed. Where we decline or disagree we explain this in the response.

Reviewer #1 (Recommendations For The Authors):

• How was the FDR < 0.003 cutoff chosen for DEG? All cutoffs are arbitrary but there should be some justification.

We agree and have provided the rationale at that point in the paper (before Figure 3) in R2: "For GO term analysis the absolute fold-change criterion was ≥ 2. Because of the ~3-fold greater number of transcripts for the M. musculus reference set than the P. leucopus reference set, application of the same false-discovery rate (FDR) threshold for both datasets would favor the labeling of transcripts as DEGs in P. leucopus. Accordingly, the FDR p values were arbitrarily set at <5 x 10-5 for P. leucopus and <3 x 10-3 for M. musculus to provide approximately the same number of DEGs for P. leucopus (1154 DEGs) and M. musculus (1266 DEGs) for the GO term comparison."

• It would be helpful to include a figure demonstrating the correlation between CD45 and WBC ("Pearson's continuous and Spearman's ranked correlations between log-transformed total white blood cell counts and normalized reads for Ptprc across 40 animals representing both species, sexes, and treatments were 0.40 (p = 0.01) and 0.34 (p = 0.03), respectively.")

In both the first version of the revision (R1) and in R2 we provide a fuller explanation of the choice of CD45 (Ptprc) for normalization as detailed in the response to Reviewer #1's public comment. In the revision only Pearson's correlation and p value is given. We did not think another figure was justified after there was additional space devoted to this in both R1 and R2.

• Unclear what the following paragraph is referring to-is this from the previous paper? Was this experiment introduced somewhere? "Low transcription of Nos2 and high transcription of Arg1 both in controls and LPS-treated P. leucopus was also observed in the experiment where the dose of LPS was 1 µg/g body mass instead of 10 µg/g and the interval between injection and assessment was 12 h instead of 4 h (Table 4)."

This experiment is described in the Methods in the original and subsequent versions, but we agree that it is not clear whether it was from present study or previous one. Here is the revised text for R2: "Low transcription of Nos2 in both in controls and LPS-treated P. leucopus and an increase in Arg1 with LPS was also observed in another experiment for the present study where the dose of LPS was 1 µg/g body mass instead of 10 µg/g and the interval between injection and assessment was 12 h instead of 4 h (Table 4)."

• Regarding the differences in IFNy between outbred and BALB/c mice-are there any other RNA-seq datasets you can mine where other inbred mice (B/6, C3H, etc) have been injected with LPS and probed roughly the same amount of time later? Do they look like BALB/c or the outbreds?

In both the original and R1 and R2 we cite two papers on the difference of BALB/c mice. While this is of interest for follow-up in the future, we did not think additional content on a subject that mainly pertains to M. musculus was warranted here, where the main focus is Peromyscus.

• Figure 8 and its legend are difficult to follow. The top half of the figure is not well explained and it's unclear what species this is. Decreased use of abbreviations would help. Consider marking each R2 value as Mus or Peromyscus (As done in Fig 9). There are some typographical errors in the legend ("gree," incomplete sentence missing the words LPS or treatment AND Mus: "Co-variation between transcripts for selected PRRs (yellow) and ISGs (gree) in the blood of P. leucopus (P) or (M) with (L") or without (C)."

This is now Figure 9 in both R1 and R2. We revised it for R1 to include references to the box plots in supplementary materials, but agree with Reviewer #1's recommendation to correct the typos and make the legend less confusing. We did not think that further labeling of the R2 values in the scatterplots with the species names was necessary. The data points are not just colors but also different symbols, so it should be fairly easy for readers to distinguish the regression lines by species. For R2 this is the revised legend with additions in response to the recommendation underlined:

"Figure 9. Co-variation between transcripts for selected PRRs and ISGs in the blood of P. leucopus (P) or M. musculus (M) with (L) or without (C) LPS treatment. Top panel: matrix of coefficients of determination (R2) for combined P. leucopus and M. musculus data. PRRs are indicated by yellow fill and ISGs by blue fill on horizontal and vertical axes. Shades of green of the matrix cells correspond to R2 values, where cells with values less than 0.30 have white fill and those of 0.90-1.00 have deepest green fill. Bottom panels: scatter plots of log-transformed normalized Mx2 transcripts on Rigi (left), Ifih1 (center), and Gbp4 (right). The linear regression curves are for each species. For the right-lower graph the result from the General Linear Model (GLM) estimate is also given. Values for analysis are in Table S4; box plots for Gbp4, Irf7, Isg15, Mx2, and Oas1 are provided in Figure S6."

• Discussion section could benefit from editing for clarity. Examples listed: o Unclear what effect is described here "The bacterial infection experiment indicated that the observed effect in P. leucopus was not limited to a TLR4 agonist; the lipoproteins of B. hermsii are agonists for TLR2 (Salazar et al. 2009)."

Both R1 and R2 include the new section on the B. hermsii infection model. This was added in response to Reviewer #1 public comment. So the expanded consideration of this aspect should address the reviewer's recommendation for more clarity and context here. For R2 we modified the text in the discussion of R1:

"The analysis here of the B. hermsii infection experiment also indicated that the phenomenon observed in P. leucopus was not limited to a TLR4 agonist."

o Unclear what the takeaway from this paragraph is: "Reducing the differences between P. leucopus and the murids M. musculus and R. norvegicus to a single all-embracing attribute may be fruitless. But from a perspective that also takes in the 2-3x longer life span of the whitefooted deer mouse compared to the house mouse and the capacity of P. leucopus to serve as disease agent reservoir while maintaining if not increasing its distribution (Moscarella et al. 2019), the feature that seems to best distinguish the deer mouse from either the mouse or rat is its predominantly anti-inflammatory quality. The presentation of this trait likely has a complex, polygenic basis, with environmental (including microbiota) and epigenetic influences. An individual's placement is on a spectrum or, more likely, a landscape rather than in one or another binary or Mendelian category."

We agree that modification, simplication, and clarification was called for. In response to a public comment of Reviewer #1 we had changed that section, leaving out reference to longevity here. Here is the revised text in both R1 and R2:

"Reducing differences between P. leucopus and murids M. musculus and R. norvegicus to a single attribute, such as the documented inactivation of the Fcgr1 gene in P. leucopus (7), may be fruitless. But the feature that may best distinguish the deermouse from the mouse and rat is its predominantly anti-inflammatory quality. This characteristic likely has a complex, polygenic basis, with environmental (including microbiota) and epigenetic influences. An individual’s placement is on a spectrum or, more likely, a landscape rather than in one or another binary or Mendelian category."

Minor comments:

• Use of blue and red in figures as the -only- way to easily distinguish between groups is a poor choice-both in terms of how inclusivity of color-blind researchers and enabling grayscale printing. Most detrimental in Figure 2, but also slightly problematic in Figure 1. Use of color and shape (as done in other figures) is a much better alternative.

We agree. Both figures have been modified to include an additional characteristic for denoting the data point. For Figure 1 it is a black filling, and for Figure 2 it is the size of symbol in additon to the color. This should enable accurate visualization by color blind individuals and printing in gray scale. We have added definitions for the symbols within the graph itself, so there is no need to refer to the legend to interpret what they mean.

• Note the typo where it should read P leucopus: "The differences between P. musculus and M. musculus in the ratios of Nos2/Arg1 and IL12/IL10 were reported before (BalderramaGutierrez et al. 2021),"

We thank the reviewer for pointing this typo out, which also carried over to R1. It has been corrected for R2.

• Optional: Can the relationship between the ratios in figure 5 and macrophage "types" be displayed graphically alongside the graphs? It's a little challenging to go back and forth between the text and the figure to try to understand the biological implication.

We considered something like this but in the end decided that we were not yet comfortable assigning “types” in this fashion for Peromyscus.

Reviewer #2 (Recommendations For The Authors):

• Be consistent with nomenclature for your species/treatment groups in the text, figures, and tables. For example, you go back and forth between "P. leucopus" and "deermouse" in the text. And in figures you use "P," "Peromyscus", or "Pero".

In the Methods section of the original and revisions R1 and R2 we indicate that "deermouse" is synonymous with "Peromyscus leucopus" and "mouse" is synonymous with "Mus musculus" in the context of this paper. We think that some alternation in the terms relieves the text of some of its repetitiveness and that readers should not have a problem with equating one with the other. The use of "deermouse" also reinforces for readers that Peromyscus is not a mouse. With regard to the abbreviations for P. leucopus, those were used to accommodate design and space issues of the figures or tables. In all cases, the abbreviations referred to are defined in the legends of the figures. So, we respectfully decline to follow this recommendation.

• Often the sentence structure and/or word choice is irregular and makes quick/easy comprehension difficult. Several examples are:

o The third paragraph of the introduction

We agree that the first and second sentences are unclear. Here is the revision for R2:

“As a species native to North America, P. leucopus is an advantageous alternative to the Eurasian-origin house mouse for study of natural variation in populations that are readily accessible (9, 53). A disadvantage for the study of any Peromyscus species is the limited reagents and genetic tools of the sorts that are applied for mouse studies.”

o The first line after Figure 5 on page 9.

We agree. The long sentence which we think the reviewer is referring to has been in split into two sentences for R2.

“An ortholog of Ly6C (13), a protein used for typing mouse monocytes and other white cells, has not been identified in Peromyscus or other Cricetidae family members. Therefore, for this study the comparison with Cd14 is with Cd16 or Fcgr3, which deermice and other cricetines do have.”

o The sentence that starts "Our attention was drawn to..." on page 14.

We agree that the sentence was awkward and split into two sentences.

“Our attention was drawn to ERVs by finding in the genome-wide RNA-seq of LPS-treated and control rats. Two of the three highest scoring DEGs by FDR p value and fold-change were a gagpol polyprotein of a leukemia virus with 131x fold-change from controls and a mouse leukmia virus (MLV) envelope (Env) protein with 62x fold-change (Dryad Table D5).”

• For figures with multiple panels, use A), B) etc then indicate which panel you are discussing in your text. This is a very data heavy study and your readers can easily get lost.

We agree and have added pointers in the text to the panels we are referring to. But we prefer to use easily understood descriptors like “left” and “upper” over assigned letters.

• For all the figures, where are the stats from the t-tests? Why didn't you do a two-way ANOVA? Instead of multiple t-tests?

Where we are not hypothesis testing and we are able to show all the data points in box-whisker plots with distributions fully revealed, our default position is not to apply significance tests in a post hoc fashion. If a reader or other investigator wants to do this for other purposes, e.g. a meta-analysis, the data is provided in public repository for them to do this. We are not sure what the reviewer means by "multiple t-tests" for "all figures". Where we do 2-tailed t-tests for presentation of data for many genes in a table for the targeted RNA (where individual values cannot shown in the table), there is always correction for multiple testing, as indicated in Methods. The p values shown as "FDR" are after correction.

• Results paragraph "LPS experiment and hematology studies"

o List the two species for the first description to orient the reader since you eventually include rat data.

We agree that this is warranted and followed this recommendation for R2.

o Not all the mice experienced tachypnea, but the text makes it seem like 100% did.

We are not sure what the reviewer is referring to here. This is what is in the text on tachypnea: "By the experiment’s termination at 4 h, 8 of 10 M. musculus treated with LPS had tachypnea, while only one of ten LPS-treated P. leucopus displayed this sign of the sepsis state (p = 0.005)." The only other mention of "tachypnea" was in Methods.

• Figure 1: Why was the M. musculus outlier excluded? Where any other outliers excluded?

That data point for the mouse was not "excluded" from the graph. It is identified (MM17) for reference with Table 1, and there is the graph for all to see where it is. It was only excluded from the regression curve for control mice. There was no significance testing. There were no other outliers excluded.

• Figure 3: explain the colors and make the scales the same for all the panels or at least for the upregulated DEGs and the downregulated DEGs.

We have modified the legend for Figure 3 to include fuller definitions of the x-axes and a description of the color spectrum. We decline to make the x-axis scale the same for all the panels because the horizontal bars in “transcription down” panels would take up only a small fraction of the space. The x-axes are clearly defined and the colors of the bars also indicate the differences in p-values. We doubt that readers will be misled. Here is the revised legend: “Figure 3. Gene Ontology (GO) term clusters associated with up-regulated genes (upper panels) and down-regulated genes (lower panels) of P. leucopus (left panels) and M. musculus (right panels) treated with LPS in comparison with untreated controls of each species. The scale for the x-axes for the panels was determined by the highest -log10 p values in each of the 4 sets. The horizontal bar color, which ranges from white to dark brown through shades of yellow through orange in between, is a schematic representation of the -log10 p values.”

• Results paragraph "Targeted RNA seq analysis"

o In the third paragraph, an R2 of 0.75 is not close enough to 1 to call it "~1"

What the reviewer is referring to is no longer in either R1 and R2, as detailed in the authors' response to public comments.

o In the 4th paragraph, where are your stats?

We have replaced terms like "substantially" and "marginally" with simple descriptions of relationships in the graphs.

"For the LPS-treated animals there was, as expected for this selected set, higher expression of the majority genes and greater heterogeneity among P. leucopus and M. musculus animals in their responses for represented genes. In contrast to the findings with controls, Ifng and Nos2 had higher transcription in treated mice. In deermice the magnitude of difference in the transcription between controls and LPS-treated was less."

• Figure 4: The colors are hard to see, I suggest making all the up regulated reads one color, the down regulated reads a different color, and the reads that aren't different black or gray.

This is now Figure 5 in R1 and R2. The selected genes that are highlighted in the panels are denoted not only by color but also by type of symbol. We do not think that readers will have a problem telling one from another even if color blind. The purpose of this figure was to provide an overview and a visual representation with calling out of selected genes, some of which will be evaluated in more detail later. We thought that this was necessary before diving deeper into the data of Table 2. We do not think further discriminating between transcripts in the categorical way that the reviewer suggests is warranted at this point. So, we respectfully decline to follow this suggestion.

• Results paragraph " Alternatively- activated macrophages...."

o Include a brief description of Nos2 and Arg1

We have defined what enzymes these are genes for in R2.

o How do you explain the lack of a difference in P. leucopus Arg1? Your text says the RT-qPCR confirms the RNA-seq findings.

There was a difference in P. leucopus Arg1 by RT-qPCR between control and LPS treated by about 3-fold. By both RNA-seq and RT-qPCR Arg1 transcription is higher in P. leucopus than in M. musculus under both conditions. But we have modified the sentence so that does not imply more than what the data and analysis of the table reveal.

"While we could not type single cells using protein markers, we could assess relative transcription of established indicators of different white cell subpopulations in whole blood. The present study, which incorporated outbred M. musculus instead of an inbred strain, confirmed the previous finding of differences in Nos2 and Arg1 expression between M. musculus and P. leucopus (Figure 5; Table 2). Results similar to the RNA-seq findings were obtained with specific RT-qPCR assays for Nos2 and Arg1 transcripts for P. musculus and M. musculus (Table 3)."

• Figure 5: reorganize the panels to make the text description and label with letters, where are the stats?

We thought the figure (now Figure 6) was self-explanatory, but agree that further explanation in the legend was indicated. We prefer to use descriptions of locations (“upper left”) over labels, like “panel C”, which do not obviously indicate the location of the panel. Of course, if the journal’s style mandates the other format we will do so. Our response about “stats” for boxplot figures is the same as what we provided above.

• Results paragraph "Interferon-gamma and interleukin-1 beta..."

o Either add the numbers or direct the viewer to where Ifng is in Table 2. The table is very big and Ifng is all the way at the bottom!

We agree that this table is large, but we thought it better to err on the side of inclusiveness by having a single table, rather than have some genes in the main article and other results in a supplementary table. We thought that it would make it easier for reviewers and readers to find a gene of interest, but we also acknowledge the challenge to locate the genes we highlight. We follow for R2 that reviewer's recommendation to provide some guidance for readers trying to locate a featured gene by pointing relative locations. While adding a column of numbers to already complex table seems more than what is called for, we are depositing an Excel spreadsheet of the table at the Dryad repository to facilitate searching by an interested reader for a particular gene.

• Figure 6: stats? The pink and red are hard to easily distinguish from each other. I also suggest not using red and green together for color blind readers.

With regard to the box-plots and significance testing, please see response above to an earlier recommendation. We have removed an interpretative adjective (i.e. "marked") from the description of the graph. Different symbols as well as colors are used, so we do not think that this will pose a problem for readers, even those with complete red-green color blindness. For what it’s worth, with regard to the "red" and "pink" issue, according to the figure on our displays the colors of the two symbols appear to be red and purple. They are also applied to different species and different conditions for those species.

• Figure 8: In the legend it says "... PRRs (yellow) and ISGs (gree)" which is a typo, but don't you mean blue not green anyways?

See response above to Reviewer #1's recommendation. This has been corrected.

Reviewer #1 (Public Review):

Summary:<br /> This paper examines patterns of diversity and divergence in two closely related sub-species of Zea mays. While the patterns are interesting, the strength of evidence in support of the conclusions drawn from these patterns is weak overall. Most of the main conclusions are not supported by convincing analyses.

Strengths:<br /> The paper presents interesting data from sets of sympatric populations of the two sub-species, maize and teosinte. This sampling offers unique insights into the diversity and divergence between the two, as well as the geographic structure of each.

Weaknesses:<br /> There were issues with many parts of the paper, especially with the strength of conclusions that can be drawn from the analyses. I list the major issues in the order in which they appear in the paper.

1. Gene flow and demography.<br /> The f4 tests of introgression (Figure 1E) are not independent of one another. So how should we interpret these: as gene flow everywhere, or just one event in an ancestral population? More importantly, almost all the significant points involve one population (Crucero Lagunitas), which suggests that the results do not simply represent gene flow between the sub-species. There was also no signal of increased migration between sympatric pairs of populations. Overall, the evidence for gene flow presented here is not convincing. Can some kind of supporting evidence be presented?

The paper also estimates demographic histories (changes in effective population sizes) for each population, and each sub-species together. The text (lines 191-194) says that "all histories estimated a bottleneck that started approximately 10 thousand generations ago" but I do not see this. Figure 2C (not 2E, as cited in the text) shows that teosinte had declines in all populations 10,000 generations ago, but some of these declines were very minimal. Maize has a similar pattern that started more recently, but the overall species history shows no change in effective size at all. There's not a lot of signal in these figures overall.

I am also curious: how does the demographic model inferred by mushi address inbreeding and homozygosity by descent (lines 197-202)? In other words, why does a change in Ne necessarily affect inbreeding, especially when all effective population sizes are above 10,000?

2. Proportion of adaptive mutations.<br /> The paper estimates alpha, the proportion of nonsynonymous substitutions fixed by positive selection, using two different sampling schemes for polymorphism. One uses range-wide polymorphism data and one uses each of the single populations. Because the estimates using these two approaches are similar, the authors conclude that there is little local adaptation. However, this conclusion is not justified.

There is little information as to how the McDonald-Kreitman test is carried out, but it appears that polymorphism within either teosinte or maize (using either sampling scheme) is compared to fixed differences with an outgroup. These species might be Z. luxurians or Z. diploperennis, as both are mentioned as outgroups. Regardless of which is used, this sampling means that almost all the fixed differences in the MK test will be along the ancestral branch leading to the ancestor of maize or teosinte, and on the branch leading to the outgroup. Therefore, it should not be surprising that alpha does not change based on the sampling scheme, as this should barely change the number of fixed differences (no numbers are reported).

The lack of differences in results has little to do with range-wide vs restricted adaptation, and much more to do with how MK tests are constructed. Should we expect an excess of fixed amino acid differences on very short internal branches of each sub-species tree? It makes sense that there is more variation in alpha in teosinte than maize, as these branches are longer, but they all seem quite short (it is hard to know precisely, as no Fst values or similar are reported).

3. Shared and private sweeps.<br /> In order to make biological inferences from the number of shared and private sweeps, there are a number of issues that must be addressed.

One issue is false negatives and false positives. If sweeps occur but are missed, then they will appear to be less shared than they really are. Table S3 reports very high false negative rates across much of the parameter space considered, but is not mentioned in the main text. How can we make strong conclusions about the scale of local adaptation given this? Conversely, while there is information about the false positive rate provided, this information doesn't tell us whether it's higher for population-specific events. It certainly seems likely that it would be. In either case, we should be cautious saying that some sweeps are "locally restricted" if they can be missed more than 85% of the time in a second population or falsely identified more than 25% of the time in a single population.

A second, opposite, issue is shared ancestral events. Maize populations are much more closely related than teosinte (Figure 2B). Because of this, a single, completed sweep in the ancestor of all populations could much more readily show a signal in multiple descendant populations. This is consistent with the data showing more shared events (and possibly more events overall). There also appear to be some very closely (phylogenetically) related teosinte populations. What if there's selection in their shared ancestor? For instance, Los Guajes and Palmar Chico are the two most closely related populations of teosinte and have the fewest unique sweeps (Figure 4B). How do these kinds of ancestrally shared selective events fit into the framework here?

These analyses of shared sweeps are followed by an analysis of sweeps shared by sympatric pairs of teosinte and maize. Because there are not more events shared by these pairs than expected, the paper concludes that geography and local environment are not important. But wouldn't it be better to test for shared sweeps according to the geographic proximity of populations of the same sub-species? A comparison of the two sub-species does not directly address the scale of adaptation of one organism to its environment, and therefore it is hard to know what to conclude from this analysis.

4. Convergent adaptation<br /> My biggest concern involves the apparent main conclusion of the paper about the sources of "convergent adaptations". I believe the authors are misapplying the method of Lee and Coop (2017), and have not seriously considered the confounding factors of this method as applied. I am unconvinced by the conclusions that are made from these analyses.

The method of Lee and Coop (referred to as rdmc) is intended to be applied to a single locus (or very tightly linked loci) that shows adaptation to the same environmental factor in different populations. From their paper: "Geographically separated populations can convergently adapt to the same selection pressure. Convergent evolution at the level of a gene may arise via three distinct modes." However, in the current paper, we are not considering such a restricted case. Instead, genome-wide scans for sweep regions have been made, without regard to similar selection pressures or to whether events are occurring in the same gene. Instead, the method is applied to large genomic regions not associated with known phenotypes or selective pressures.

I think the larger worry here is whether we are truly considering the "same gene" in these analyses. The methods applied here attempt to find shared sweep regions, not shared genes (or mutations). Even then, there are no details that I could find as to what constitutes a shared sweep. The only relevant text (lines 802-803) describes how a single region is called: "We merged outlier regions within 50,000 Kb of one another and treated as a single sweep region." (It probably doesn't mean "50,000 kb", which would be 50 million bases.) However, no information is given about how to identify overlap between populations or sub-species, nor how likely it is that the shared target of selection would be included in anything identified as a shared sweep. Is there a way to gauge whether we are truly identifying the same target of selection in two populations?

The question then is, what does rdmc conclude if we are simply looking at a region that happened to be a sweep in two populations, but was not due to shared selection or similar genes? There is little testing of this application here, especially its accuracy. Testing in Lee and Coop (2017) is all carried out assuming the location of the selected site is known, and even then there is quite a lot of difficulty distinguishing among several of the non-neutral models. This was especially true when standing variation was only polymorphic for a short time, as is estimated here for many cases, and would be confused for migration (see Lee and Coop 2017). Furthermore, the model of Lee and Coop (2017) does not seem to consider a completed ancestral sweep that has signals that persist into current populations (see point 3 above). How would rdmc interpret such a scenario?

Overall, there simply doesn't seem to be enough testing of this method, nor are many caveats raised in relation to the strange distributions of standing variation times (bimodal) or migration rates (opposite between maize and teosinte). It is not clear what inferences can be made with confidence, and certainly the Discussion (and Abstract) makes conclusions about the spread of beneficial alleles via introgression that seem to outstrip the results.

During the time that Shakespeare wrote Hamlet, there was a lot of uncertainty in England. With Elizabeth I reign coming to an end, and with no heir named, there was a lot of unease and uncertainty. “Claudius has hastily married the queen in order to secure his claim, and the old kings son, Hamlet, is openly unhappy about it” (Queen Elizabeths Decline). I think we can see this in the way that Hamlet speaks of the unrest of his kingdom after his uncle takes over the reign. “Queen Elizabeths Decline.”Sparknotes,Sparknotes,www.sparknotes.com/Shakespeare/hamlet/context/historical/queen-Elizabeth’s-decline/.

Author Response

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

We thank the reviewers for their positive remarks. We have addressed the reviewers’ recommendations in the point-by-point response below to improve our revised manuscript.

Reviewer #1 (Recommendations For The Authors):

1. The authors carry out their HDX-MS work on Prestin (and SLC26A9) solubilized in glycol-diosgenin. The authors should carefully rationalize their choice of detergent and discuss how their key findings are also pertinent to the native state of Prestin when residing in an actual phospholipid bilayer. More native membrane mimetic models are available, for instance, nano-discs etc. While I am not insisting that the authors have to repeat their measurements in a more native membrane system, it would be a very nice control experiment, and in any case, a detailed discussion of the limitations of the approach taken and possible caveats should be included - possibly with additional references to other studies.

Response: We have added a paragraph rationalizing the choice of detergent in lines 174-176. We have also added requested HDX data comparing prestin reconstituted in nanodisc to prestin solubilized in micelle (Fig 5). The HDX for prestin under these two membrane mimetics were indistinguishable, including the anion-binding site, suggesting that our major findings are likely pertinent to prestin residing in a lipid bilayer. The only major HDX difference we observed was that a lipid-facing helix TM6 is more dynamic for prestin in nanodisc compared to in micelles. In our previous structural studies, we identified TM6 as the “eletromotile elbow” that is important for prestin’s mechanical expansion (Bavi et al., Nature, 2021). We are currently conducting a more thorough investigation to understand the role of TM6 in prestin’s electromotility.

1. As far as I understand, the HEPES state represents the apo-state and thus assumes that HEPES does not bind to Prestin - the authors should support this assumption or include a discussion of the possible effect of HEPES on Prestin. Also, the HEPES state has fewer time-points - this should also be discussed.

Response: We have included a discussion of the possible effects of HEPES in lines 331-345. In fact, in an attempt to support our assumption that HEPES does not bind to prestin, we set out to determine the structure of prestin in the HEPES-based buffer using single particle cryo-EM. However, we did not find evidence that HEPES binds to prestin. Details are discussed in lines 331-345 and Supporting Information Text 3.

We employed a denser sampling of HDX labeling times for prestin in Cl- because it is critical for fitting and ∆G calculation. The earlier time points are used mainly to evaluate the dynamics of the less stable cytosolic domain. Since the cytosolic domain does not directly participate in prestin’s voltage-sensing mechanism and electromotility, we only measured the HEPES states with longer time points which mainly probe the dynamics of the transmembrane domain.

1. Overall, the HDX-MS data provided and the statistical analysis done is in my view sufficiently detailed and well done - the authors are advised to make reference to and include a HDX Summary table and HDX Data Table according to the HDX-MS community-guidelines (Masson et al. Nature Methods 2019).

Response: An HDX summary table was provided in Table S1 and referred in lines 81 and 388. We have included a reference to Masson et al., Nature Methods, 2019, in line 389.

1. Figure 5 - I like the detailed analysis of the helix folding - but in my experience, one can provide a great fit of many HDX curves to a 4 -term exponential function - I think the authors would need more time-points to provide a more convincing case. But it does provide a compelling theory - even if the data strictly does not prove it. The authors should discuss this in more detail - including limitations etc.

Response: We presented a statistical analysis describing the accuracy of the fitting in Fig 6A. We acknowledge that the values of the exponentials may not be precisely determined, but the fundamental result is robust – TM3 exchanges through fraying from the N-terminal end of the helix while TM6 exchanges much more cooperatively. Collecting additional time points may reduce the error on the rates but would not contribute to additional mechanistic insights.

Reviewer #2 (Recommendations For The Authors):

1. I suggest toning down more speculative/ hypothetical aspects. Specifically, I believe that the following sentence should not be in the abstract in its present form: "This event shortens the TM3-TM10 electrostatic gap, thereby connecting the two helices such that TM3-anion-TM10 is pushed upwards by forces from the electric field, resulting in reduced cross-sectional area."

Response: The sentence has been rephrased.

1. The "nuance" between helix fraying and helix unfolding is an important aspect of the author's hypothesis but this should be explained better. In that regard, have the authors performed HDX-MS analysis of the mutant P136T? That would nicely support their claim regarding the importance of helix fraying as being foundational to allow electromotility.

Response: More explanation for helix fraying and unfolding has been provided in the main text. We have not performed HDX-MS analysis of the mutant P136T. However, we performed molecular dynamics simulations using Upside, and consistently, showed that a P136T mutation in prestin results in a highly stabilized TM3 (Fig. S4B).

1. Why do measurements at two pDs? Did the authors observe any differences?

Response: The purpose of two pDs is to increase the effective dynamic range of the HDX measurement by two orders of magnitude because the intrinsic exchange rate scales with pD & Temp. This allows us to determine the stability of both the highly and minimally stable regions within the protein. We have rephrased lines 83-87 to better rationalize this choice of pDs. With the time points performed in this study, we did not observe noticeable differences for HDX performed under the two pDs when corrected for the changes in the intrinsic rates (Fig. S7A).

1. I can't help but wonder what is the interest in doing HDX-MS measurements after 27h of incubation. Membrane proteins are known for their instability once purified and a few odd HDX profiles at that specific timepoint (especially in the 80-100 residues area) make one question whether local unfolding preceding aggregation could happen. This actually weakens the author's claims about cooperative unfolding and localized and directional helix fraying. Could they provide some evidence (CD, thermostability measurements such as trp fluorescence quenching, or SEC analysis) that the prestin is still folded after 27h in GDN.

Response: We appreciate reviewer’s comments on membrane proteins can be unstable once purified. In our system, we did not observe evidence of unfolding or aggregation caused by long-term incubation after purification. This is mostly supported by the fact that our HDX reactions were initiated and injected to MS in random order, yet are still highly reproducible among biological and technical replicates. A specific example included HDX on freshly purified SLC26A9 gave the same deuteration levels as SLC26A9 purified in GDN after 4 days. For prestin, although we don’t have direct comparison between fresh samples and old samples (24-27h post-purification) due to the lack of samples, 30s HDX in SO42- performed 24h post-purification gave a %D that fell between 10s and 90s of labeling done on fresh sample. Additionally, HDX on prestin in Cl- performed on freshly purified sample gave the sample %D as prestin in the presence of 1M urea labeled after 24~48h of purification, suggesting that prestin is relatively resistant to aggregation at least within 48h after purification even in the presence of 1 M urea (data not shown).

Furthermore, the HDX for prestin in nanodisc are essentially identical to prestin in micelles except for a functionally important helix (TM6), suggesting minimal aggregation or misfolding.

We think the “a few odd HDX profiles” at 27h time points for residues 80-100 are caused by two reasons. Firstly, TM1 unfolds cooperatively and its stability in HEPES falls within the detection range when long labeling time points were employed (within one log unit of 27h). Secondly, we observed two non-interconverting and structurally distinct populations for TM1 (Supporting Information Text 1 & Fig. S8), and in long labeling times, the two isotope distributions merge and sometimes can skew the %D calculations. Nevertheless, the HDX differences we observed comparing across conditions are clear and such %D calculation skewing, if present, should be minimal and does not change our main conclusions.

Author Response

The following is the authors’ response to the previous reviews

Point-to-Point Responses to Reviewers’ Comments

We are a bit surprised by the comments of Reviewer 1, but that our further responses can help communications with Reviewer 1. We have also responded to comments of Reviewers 2 and 3.

Public Reviews:

*Reviewer #1 (Public Review):

The overall tone of the rebuttal and lack of responses on several questions was surprising. Clearly, the authors took umbrage at the phrase 'no smoking gun' and provided a lengthy repetition of the fair argument about 'ticking boxes' on the classic list of criteria. They also make repeated historical references that descriptions of neurotransmitters include many papers, typically over decades, e.g. in the case of ACh and its discovery by Sir Henry Dale. While I empathize with the authors' apparent frustration (I quote: '...accept the reality that Rome was not built in a single day and that no transmitter was proven by a one single paper') I am a bit surprised at the complete brushing away of the argument, and in fact the discussion. In the original paper, the notion of a receptor was mentioned only in a single sentence and all three reviewers brought up this rather obvious question. The historical comparisons are difficult: Of course many papers contribute to the identification of a neurotransmitter, but there is a much higher burden of proof in 2023 compared to the work by Otto Loewi and Sir Henry Dale: most, if not all, currently accepted neurotransmitter have a clear biological function at the level of the brain and animal behavior or function - and were in fact first proposed to exist based on a functional biological experiment (e.g. Loewi's heart rate change). This, and the isolation of the chemical that does the job, were clear, unquestionable 'smoking guns' a hundred years ago. Fast forward 2023: Creatine has been carefully studied by the authors to tick many of the boxes for neurotransmitters, but there is no clear role for its function in an animal. The authors show convincing effects upon K+ stimulation and electrophysiological recordings that show altered neuronal activity using the slc6a8 and agat mutants as well as Cr application - but, as has been pointed out by other reviewers, these effects are not a clear-cut demonstration of a chemical transmitter function, however many boxes are ticked. The identification of a role of a neurotransmitter for brain function and animal behavior has reasonably more advanced possibilities in 2023 than a hundred years ago - and e.g. a discussion of approaches for possible receptor candidates should be possible.

Again, I reviewed this positively and agree that a lot of cumulative data are great to be put out there and allow the discovery to be more broadly discussed and tested. But I have to note, that the authors simply respond with the 'Rome was not built in a single day' statement to my suggestions on at least 'have some lead' how to approach the question of a receptor e.g. through agonists or antagonists (while clearly stating 'I do not think the publication of this manuscript should not be made dependent' on this). Similarly, in response to reviewer 2's concerns about a missing receptor, the authors' only (may I say snarky) response is ' We have deleted this sentence, though what could mediate postsynaptic responses other than receptors?' The bullet point by reviewer 3 ' • No candidate receptor for creatine has been identified postsynaptically.' is the one point by that reviewer that is simply ignored by the authors completely. Finally, I note that my reivew question on the K stimulation issues (e.g. 35 neurons that simply did not respond at all) was: ' Response: To avoid the disadvantage of K stimulation, we also performed optogenetic experiments recently and obtained encouraging preliminary results.' No details, not data - no response really.

In sum, I find this all a bit strange and the rebuttal surprising - all three reviewers were supportive and have carefully listed points of discussion that I found all valid and thoughtful. In response, the authors selectively responded scientifically to some experimental questions, but otherwise simply rather non-scientifically dismissed questions with 'Rome was not built in a day'-type answers, or less. I my view, the authors have disregarded the review process and the effort of three supportive reviewers, which should be part of the permanent record of this paper.

Response:

We were very surprised by the tone of Reviewer 1 in the second round of reviewing. The corresponding author has spent some time including a long holiday to cool down and re-read our earlier responses. The following is entirely by the correspond author.

I have finally checked the term “smoking gun”, and found out that I interpreted it wrongly while I had thought that Reviewer 1 was wrong. This came from a long story in that I was lectured by a native speaker for my English when submitting the first paper from my own paper. In that case, the Reviewer was wrong (in arguing that only adjectives but not nouns can be used to define nouns), I was quite offended and remembered it vividly. In the case of “smoking gun”, I wrongly believed that it meant a hint (while the definite evidence would be “the final nail in the coffin”). By interpreting is as a hint, I was then rebutting Reviewer 1 for negating all our experimental results as “not a single piece of suggestive evidence”.

For the above, I apologize.

I have another disagreement about “smoking gun”. For a transmitter, multiple criteria have to be met. For example, finding a receptor for a small molecule would not be definitive for a transmitter because if it is not present in the SVs, it is unlikely to be a typical transmitter. If a molecule has a receptor but they are not even in the nervous system, it is definitely no a transmitter.

The title of our paper is “Evidence suggesting creatine as a new central neurotransmitter”, not “Evidence proving creatine as a new central neurotransmitter”. In the Abstract, after “Our biochemical, chemical, genetic and electrophysiological results are consistent with the possibility of Cr as a neurotransmitter”, we are adding “though not yet reaching the level of proof for the now classic transmitters”. In the last sentence of the introduction, we have now added “though the discovery of a receptor for Cr would prove it”.

I do, however, believe that, however strong the wordings are, criticisms and rebuttals in science are normal and should be conducted even when emotions are involved.

One of my major point of differences with at least two of the reviewers is that the criteria for neurotransmitters should be those listed in major textbooks. While everyone can have one’s own opinions, the textbooks, especially those accepted by readers of the field for more than 40 years, should be the standards. Kandel has listed the 4 criteria not only 40 years ago but also just 2 years ago in their latest 6th edition. The reviewers have asked for more, while discounting Kandel et al. (2021). So, in essence, the Reviewer is not shy in scientific criticisms when stating “The identification of a role of a neurotransmitter for brain function and animal behavior has reasonably more advanced possibilities in 2023 than a hundred years ago”.

Reviewer 1 raised another new criterion: brain function and behavior, while this is not in any textbook lists. However, lack of Cr caused behavioral problems, as cited by us in the introduction: both humans and mice were defective in brain function with loss of function mutations in the gene for the specific Cr transporter SLC6A8. If the reviewer meant behavioral abnormalities caused by Cr injection, that was unclear. But that criterion may not be met by other transmitters which is the likely reason that it was not a criterion in any textbook.

Reviewer #2 (Public Review):

Summary:

Bian et al studied creatine (Cr) in the context of central nervous system (CNS) function. They detected Cr in synaptic vesicles purified from mouse brains with anti-Synaptophysin using capillary electrophoresis-mass spectrometry. Cr levels in the synaptic vesicle fraction was reduced in mice lacking the Cr synthetase AGAT, or the Cr transporter SLC6A8. They provide evidence for Cr release within several minutes after treating brain slices with KCl. This KCl-induced Cr release was partially calcium dependent and was attenuated in slices obtained from AGAT and SLC6A8 mutant mice. Cr application also decreased the excitability of cortical pyramidal cells in one third of the cells tested. Finally, they provide evidence for SLC6A8-dependent Cr uptake into synaptosomes, and ATP-dependent Cr loading into synaptic vesicles. Based on these data, the authors propose that Cr may act as neurotransmitter in the CNS.

Strengths: 1. A major strength of the paper is the broad spectrum of tools used to investigate Cr. 2. The study provides evidence that Cr is present in/loaded into synaptic vesicles.

Weaknesses: 1. There is no significant decrease in Cr content pulled down by anti-Syp in AGAT-/- mice when normalized to IgG controls. Hence, blocking AGAT activity/Cr synthesis does not affect Cr levels in the synaptic vesicle fraction, arguing against a Cr enrichment.

Response: Evidence for Cr enrichment in the SVS was obtained robustly with wild type mice. When brain Cr is very low in AGAT-/- mutant mice, because there is little Cr, there is also little Cr in the SVs. One does not require that as a criterion: it does not argue against the normal levels of Cr could be transported into the SVs even if when the much reduced levels of AGAT-/- Cr in mutant mice could be enriched in SVs.

1. There is no difference in KCl-induced Cr release between SLC6A8-/Y and SLC6A8+/Y when normalizing the data to the respective controls. Thus, the data are not consistent with the idea that depolarization-induced Cr release requires SLC6A8.

Response: This comment of Reviewer 2 was based on Figure 5D. But if one carefully examines Figure 5G, it was clear that the Ca++ dependent component of KCl -induced Cr release was lower in SLC6A8-/Y than that in SLC6A8+/Y.

1. The rationale of grouping the excitability data into responders and non-responders is not convincing because the threshold of 10% decrease in AP rate is arbitrary. The data do therefore not support the conclusion that Cr reduces neuronal excitability.

Response: Comparison of the same neuron, before and after Cr did show effects on neuronal excitability though that would have no statistics if one does not group multiple cells into the same categories.

Reviewer #3 (Public Review):

SUMMARY:

The manuscript by Bian et al. promotes the idea that creatine is a new neurotransmitter. The authors conduct an impressive combination of mass spectrometry (Fig. 1), genetics (Figs. 2, 3, 6), biochemistry (Figs. 2, 3, 8), immunostaining (Fig. 4), electrophysiology (Figs. 5, 6, 7), and EM (Fig. 8) in order to offer support for the hypothesis that creatine is a CNS neurotransmitter.

STRENGTHS:

There are many strengths to this study. • The combinatorial approach is a strength. There is no shortage of data in this study. • The careful consideration of specific criteria that creatine would need to meet in order to be considered a neurotransmitter is a strength. • The comparison studies that the authors have done in parallel with classical neurotransmitters is helpful. • Demonstration that creatine has inhibitory effects is another strength. • The new genetic mutations for Slc6a8 and AGAT are strengths and potentially incredibly helpful for downstream work.

WEAKNESSES: • Some data are indirect. Even though Slc6a8 and AGAT are helpful sentinels for the presence of creatine, they are not creatine themselves. Of note, these molecules themselves are not essential for making the case that creatine is a neurotransmitter.

Response: We agree, but those data are not inconsistent with the possibility.

• Regarding Slc6a8, it seems to work only as a reuptake transporter - not as a transporter into SVs. Therefore, we do not know what the transporter into the TVs is.

Response: SLC6A8 is not the transporter on the SVs, but is an excellent candidate for the transporter on the presynaptic cytoplasmic membrane for uptake of Cr into the presynaptic structure.

• Puzzlingly, Slc6a8 and AGAT are in different cells, setting up the complicated model that creatine is created in one cell type and then processed as a neurotransmitter in another. This matter will likely need to be resolved in future studies.

Response: We agree.

• No candidate receptor for creatine has been identified postsynaptically. This will likely need to be resolved in future studies.

Response: We agree.

• Because no candidate receptor has been identified, it is important to fully consider other possibilities for roles of creatine that would explain these observations other than it being a neurotransmitter? There is some attention to this in the Discussion.

Response: We agree.

There are several criteria that define a neurotransmitter. The authors nicely delineated many criteria in their discussion, but it is worth it for readers to do the same with their own understanding of the data.

By this reviewer's understanding (and combining some textbook definitions together) a neurotransmitter: 1) must be present within the presynaptic neuron and stored in vesicles; 2) must be released by depolarization of the presynaptic terminal; 3) must require Ca2+ influx upon depolarization prior to release; 4) must bind specific receptors present on the postsynaptic cell; 5) exogenous transmitter can mimic presynaptic release; 6) there exists a mechanism of removal of the neurotransmitter from the synaptic cleft.

Response: While any of us can come up with a list according to our own understanding, the paper copies lists from textbooks, especially from Kandel et al. (2021), which lists the same 4 criteria as Kandel et al. (1983), providing consistency and consensus.

For a paper to claim that the published work has identified a new neurotransmitter, several of these criteria would be met - and the paper would acknowledge in the discussion which ones have not been met. For this particular paper, this reviewer finds that condition 1 is clearly met.

Conditions 2 and 3 seem to be met by electrophysiology, but there are caveats here. High KCl stimulation is a blunt instrument that will depolarize absolutely everything in the prep all at once and could result in any number of non-specific biological reactions as a result of K+ rushing into all neurons in the prep. Moreover, the results in 0 Ca2+ are puzzling. For creatine (and for the other neurotransmitters), why is there such a massive uptick in release, even when the extracellular saline is devoid of calcium?

Response: Classic transmitters are released in a Ca++ dependent manner when stimulated by KCl, though they also had a Ca++ independent component as also shown in our Figure 5 E and F.

Condition 4 is not discussed in detail at all. In the discussion, the authors elide the criterion of receptors specified by Purves by inferring that the existence of postsynaptic responses implies the existence of receptors. True, but does it specifically imply the existence of creatinergic receptors? This reviewer does not think that is necessarily the case. The authors should be appropriately circumspect and consider other modes of inhibition that are induced by activation or potentiation of other receptors (e.g., GABAergic or glycinergic).

Response: Kandel et al. did not list this.

Condition 5 may be met, because authors applied exogenous creatine and observed inhibition. However, this is tough to know without understanding the effects of endogenous release of creatine. if they were to test if the absence of creatine caused excess excitation (at putative creatinergic synapses), then that would be supportive of the same. Nicely, Ghirardini et al., 2023 study cited by the reviewers does provide support for this exact notion in pyramidal neurons.

Response: For most commonly accepted transmitters, this criterion has never been met. For example, the simplest case would be ACh at the neuromuscular junction. Howver, we have now found that choline is clearly present in SVs. So, how does anyone be sure that only ACh is released only, or how does anyone rule out effects of choline on postsynaptic cells when cholinergic neurons are stimulated?

Many synapses are now known to release more than one transmitter, making it difficult to define the effect of one transmitter released endogenously.

These are perhaps reasons why some textbooks do not emphasize similarities of endogenously released vs exogenously applied molecules.

For condition 6, the authors made a great effort with Slc6a8. This is a very tough criterion to understand or prove for many synapses and neurotransmitters.

Response: SLC6A8 is a transporter on the cytoplasmic membrane, thus a good candidate for removal of Cr from the synaptic cleft.

In terms of fundamental neuroscience, the story should be impactful. There are certainly more neurotransmitters out there than currently identified and by textbook criteria, creatine seems to be one of them taking all of the data in this study and others into account.

Response: We hope that more will join our lonely efforts in trying to discover more transmitters.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Since the authors largely disregarded questions in the review process, I do not see a point in listing recommendation for the authors again.

Reviewer #2 (Recommendations For The Authors):

1. The different sections of the manuscript are not separated by headers.

Response: We do have separate subheadings.

1. The beginning of the results section either does not reference the underlying literature or refers to unpublished data.

Response: We have a very long introduction which was criticized for being too long and with too much historical citations. We therefore refrained from citation again in the beginning part of the Results section.

1. The text contains many opinions and historical information that are not required (e.g., "It has never been easy to discover a new neurotransmitter, especially one in the central nervous system (CNS). We have been searching for new neurotransmitters for 12 years."; l. 17).

Response: We would like to keep these because most readers are young and do not know the history and difficulties of discovering transmitters.

1. Almeida et al. (2008; doi: 10.1002/syn.20280) provided evidence for electrical activity-, and Ca2+-dependent Cr release from rat brain slices. This paper should be introduced in the introduction.

Response: Done.

1. Fig. 7: A Y-scale for the stimulation protocol is missing.

Response: Done.

Reviewer #3 (Recommendations For The Authors):

The main suggestion by this reviewer (beyond the details in the public review) was to consider the full spectrum of biology that is consistent with these results. By my reading, creatine could be a neurotransmitter, but other possibilities also exist. The authors have highlighted some of those for their Discussion.

Reviewer #1 (Public Review):

The overall tone of the rebuttal and lack of responses on several questions was surprising. Clearly, the authors did not appreciate the phrase 'no smoking gun' and provided a lengthy repetition of the fair argument about 'ticking boxes' on the classic list of criteria. They also make repeated historical references that descriptions of neurotransmitters include many papers, typically over decades, e.g. in the case of ACh and its discovery by Sir Henry Dale. While I empathize with the authors' apparent frustration (I quote: '...accept the reality that Rome was not built in a single day and that no transmitter was proven by a one single paper') I am a bit surprised at the complete brushing away of the argument, and in fact the discussion. In the original paper, the notion of a receptor was mentioned only in a single sentence and all three reviewers brought up this rather obvious question. The historical comparisons are difficult: Of course many papers contribute to the identification of a neurotransmitter, but there is a much higher burden of proof in 2023 compared to the work by Otto Loewi and Sir Henry Dale: most, if not all, currently accepted neurotransmitter have a clear biological function at the level of the brain and animal behavior or function - and were in fact first proposed to exist based on a functional biological experiment (e.g. Loewi's heart rate change). This, and the isolation of the chemical that does the job, were clear, unquestionable 'smoking guns' a hundred years ago. Fast forward 2023: Creatine has been carefully studied by the authors to tick many of the boxes for neurotransmitters, but there is no clear role for its function in an animal. The authors show convincing effects upon K+ stimulation and electrophysiological recordings that show altered neuronal activity using the slc6a8 and agat mutants as well as Cr application - but, as has been pointed out by other reviewers, these effects are not a clear-cut demonstration of a chemical transmitter function, however many boxes are ticked. The identification of a role of a neurotransmitter for brain function and animal behavior has reasonably more advanced possibilities in 2023 than a hundred years ago - and e.g. a discussion of approaches for possible receptor candidates should be possible.

Again, I reviewed this positively and agree that a lot of cumulative data are great to be put out there and allow the discovery to be more broadly discussed and tested. But I have to note, that the authors simply respond with the 'Rome was not built in a single day' statement to my suggestions on at least 'have some lead' how to approach the question of a receptor e.g. through agonists or antagonists (while clearly stating 'I do not think the publication of this manuscript should not be made dependent' on this). Similarly, in response to reviewer 2's concerns about a missing receptor, the authors' only (may I say snarky) response is ' We have deleted this sentence, though what could mediate postsynaptic responses other than receptors?' The bullet point by reviewer 3 ' • No candidate receptor for creatine has been identified postsynaptically.' is the one point by that reviewer that is simply ignored by the authors completely. Finally, I note that my reivew question on the K stimulation issues (e.g. 35 neurons that simply did not respond at all) was: ' Response: To avoid the disadvantage of K stimulation, we also performed optogenetic experiments recently and obtained encouraging preliminary results.' No details, not data - no response really.

In sum, I find this all a bit strange and the rebuttal surprising - all three reviewers were supportive and have carefully listed points of discussion that I found all valid and thoughtful. In response, the authors selectively responded scientifically to some experimental questions, but otherwise simply rather non-scientifically dismissed questions with 'Rome was not built in a day'-type answers, or less. I my view, the authors have disregarded the review process and the effort of three supportive reviewers, which should be part of the permanent record of this paper.

Reviewer #3 (Public Review):

SUMMARY:

The manuscript by Bian et al. promotes the idea that creatine is a new neurotransmitter. The authors conduct an impressive combination of mass spectrometry (Fig. 1), genetics (Figs. 2, 3, 6), biochemistry (Figs. 2, 3, 8), immunostaining (Fig. 4), electrophysiology (Figs. 5, 6, 7), and EM (Fig. 8) in order to offer support for the hypothesis that creatine is a CNS neurotransmitter.

STRENGTHS:

There are many strengths to this study.

• The combinatorial approach is a strength. There is no shortage of data in this study.<br /> • The careful consideration of specific criteria that creatine would need to meet in order to be considered a neurotransmitter is a strength.<br /> • The comparison studies that the authors have done in parallel with classical neurotransmitters is helpful.<br /> • Demonstration that creatine has inhibitory effects is another strength.<br /> • The new genetic mutations for Slc6a8 and AGAT are strengths and potentially incredibly helpful for downstream work.

WEAKNESSES:

• Some data are indirect. Even though Slc6a8 and AGAT are helpful sentinels for the presence of creatine, they are not creatine themselves. Of note, these molecules themselves are not essential for making the case that creatine is a neurotransmitter.<br /> • Regarding Slc6a8, it seems to work only as a reuptake transporter - not as a transporter into SVs. Therefore, we do not know what the transporter into the TVs is.<br /> • Puzzlingly, Slc6a8 and AGAT are in different cells, setting up the complicated model that creatine is created in one cell type and then processed as a neurotransmitter in another. This matter will likely need to be resolved in future studies.<br /> • No candidate receptor for creatine has been identified postsynaptically. This will likely need to be resolved in future studies.<br /> • Because no candidate receptor has been identified, it is important to fully consider other possibilities for roles of creatine that would explain these observations other than it being a neurotransmitter? There is some attention to this in the Discussion.

There are several criteria that define a neurotransmitter. The authors nicely delineated many criteria in their discussion, but it is worth it for readers to do the same with their own understanding of the data.

By this reviewer's understanding (and combining some textbook definitions together) a neurotransmitter: 1) must be present within the presynaptic neuron and stored in vesicles; 2) must be released by depolarization of the presynaptic terminal; 3) must require Ca2+ influx upon depolarization prior to release; 4) must bind specific receptors present on the postsynaptic cell; 5) exogenous transmitter can mimic presynaptic release; 6) there exists a mechanism of removal of the neurotransmitter from the synaptic cleft.

For a paper to claim that the published work has identified a new neurotransmitter, several of these criteria would be met - and the paper would acknowledge in the discussion which ones have not been met. For this particular paper, this reviewer finds that condition 1 is clearly met.

Conditions 2 and 3 seem to be met by electrophysiology, but there are caveats here. High KCl stimulation is a blunt instrument that will depolarize absolutely everything in the prep all at once and could result in any number of non-specific biological reactions as a result of K+ rushing into all neurons in the prep. Moreover, the results in 0 Ca2+ are puzzling. For creatine (and for the other neurotransmitters), why is there such a massive uptick in release, even when the extracellular saline is devoid of calcium?

Condition 4 is not discussed in detail at all. In the discussion, the authors elide the criterion of receptors specified by Purves by inferring that the existence of postsynaptic responses implies the existence of receptors. True, but does it specifically imply the existence of creatinergic receptors? This reviewer does not think that is necessarily the case. The authors should be appropriately circumspect and consider other modes of inhibition that are induced by activation or potentiation of other receptors (e.g., GABAergic or glycinergic).

Condition 5 may be met, because authors applied exogenous creatine and observed inhibition. However, this is tough to know without understanding the effects of endogenous release of creatine. if they were to test if the absence of creatine caused excess excitation (at putative creatinergic synapses), then that would be supportive of the same. Nicely, Ghirardini et al., 2023 study cited by the reviewers does provide support for this exact notion in pyramidal neurons.

For condition 6, the authors made a great effort with Slc6a8. This is a very tough criterion to understand or prove for many synapses and neurotransmitters.

In terms of fundamental neuroscience, the story should be impactful. There are certainly more neurotransmitters out there than currently identified and by textbook criteria, creatine seems to be one of them taking all of the data in this study and others into account.

Author Response

The following is the authors’ response to the previous reviews

eLife assessment

The manuscript offers important findings on the potential influence of maternally derived extracellular vesicles on embryo metabolism. However, while the content is convincing, the title appears to overstate the study's conclusions due to its speculative nature on the DNA transmission and embryo bioenergetics connection. A more measured title would better represent the evidence presented.

We want to extend our heartfelt appreciation to the editors and reviewers for their invaluable comments on our research. Their feedback has played a crucial role in improving the quality of our manuscript.

We acknowledge the concern regarding the manuscript's title and are fully open to making modifications. Following the recommendation of Reviewer 2, the proposed new title of the manuscript will be “Vertical transmission of maternal DNA through extracellular vesicles associates with altered embryo bioenergetics during the periconception period.”

Reviewer #1 (Public Review):

Q1. Bolumar et al. isolated and characterized EV subpopulations, apoptotic bodies (AB), Microvesicles (MV), and Exosomes (EXO), from endometrial fluid through the female menstrual cycle. By performing DNA sequencing, they found the MVs contain more specific DNA sequences than other EVs, and specifically, more mtDNA were encapsulated in MVs. They also found a reduction of mtDNA content in the human endometrium at the receptive and post-receptive period that is associated with an increase in mitophagy activity in the cells, and a higher mtDNA content in the secreted MVs was found at the same time. Last, they demonstrated that the endometrial Ishikawa cell-derived EVs could be taken by the mouse embryos and resulted in altered embryo metabolism.

This is a very interesting study and is the first one demonstrating the direct transmission of maternal mtDNA to embryos through EVs.

A1. Thank you for your kind comments.

Reviewer #2 (Public Review):

Q2. In Bolumar, Moncayo-Arlandi et al. the authors explore whether endometrium-derived extracellular vesicles contribute DNA to embryos and therefore influence embryo metabolism and respiration. The manuscript combines techniques for isolating different populations of extracellular vesicles, DNA sequencing, embryo culture, and respiration assays performed on human endometrial samples and mouse embryos.

Vesicle isolation is technically difficult and therefore collection from human samples is commendable. Also, the influence of maternally derived DNA on the bioenergetics of embryos is unknown and therefore novel. However, several experiments presented in the manuscript fail to reach statistical significance, likely due to the small sample sizes. This manuscript is a good but incomplete start as to the potential function of maternal DNA transfer via vesicles.

In my opinion the manuscript supports the following of the authors' claims:

1. Different amounts of nDNA and mtDNA are shed in human endometrial extracellular vesicles during different phases of the menstrual cycle.
2. Endometrial microvesicles are more enriched for mitochondrial DNA sequences compared to other types of vesicles present in the human samples.
3. Fluorescently labelled DNA from extracellular vesicles derived from an endometrial adenocarcinoma cell line can be incorporated into hatched mouse embryos.
4. Culture of mouse embryos with endometrial extracellular vesicles can influence embryo respiration and the effect is greater when cultured with isolated exosomes compared to other isolated microvesicles.

My main concerns with the manuscript:

1. Several experiments presented fail to reach statistical significance or are qualitative.
2. The definitive experiments presented in the manuscript are limited to the transfer of DNA in general not mtDNA. Therefore a strong connection with metabolism is missing, diminishing the significance of the findings.

A2. We thank you for your detailed feedback. While we acknowledge the reviewer's concerns regarding sample sizes, we emphasize that this study was intentionally designed as a pilot study and was approved by the IRB with a specific sample size to serve as proof of concept. We fully agree that further research is essential for a more comprehensive understanding of the novel biological process described in this manuscript. When this manuscript is finally accepted, we can submit a new IRB application to obtain a larger sample size, allowing us to delve deeper into demonstrating the connection with metabolism

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Q3. The authors have made significant improvements, and the manuscript now is appropriate for eLife.

A3. Thank you for your consideration.

Reviewer #2 (Recommendations For The Authors):

The authors have made several changes that have improved the manuscript. However, I still have some concerns.

Q4. The title is still too definitive. Something like "Vertical transmission of maternal DNA through extracellular vesicles is associated with changes in embryo bioenergetics during the periconception period" would be more appropriate.

A4. As mentioned earlier in the response to the editors, we acknowledge the concerns regarding the manuscript's title.

Following your recommendation, the proposed new title of the manuscript is “Vertical transmission of maternal DNA through extracellular vesicles associates with altered embryo bioenergetics during the periconception period.”

Q5. I am confused by the incorporation of the new experiment (supplementary figure 7) where embryos are cultured in free-floating synthesized mtDNA. If these sequences were not encapsulated in vesicles I don't think the experiment is relevant. If they were similarly prepared as in the section "Tagged-DNA production and EV internalization by murine embryos" I stand corrected but please clarify or omit. Otherwise, the new data/figure in response to Q11 showing co-localization of mitochondria and EdU-tagged DNA from MVs from Ishikawa cells is more compelling. However, this doesn't separate the uptake of mtDNA alone from the potential uptake of mitochondria, which this manuscript is not focused on.

A5. We apologize for any confusion that may have arisen for the reviewer. We conducted this experiment in response to question Q4 posed by the same reviewer, which specifically inquired about the detection of internalized mtDNA by the embryos.

As previously stated in the revised manuscript, the EdU system does not selectively label mtDNA; instead, it labels any newly synthesized DNA, both nuclear and mitochondrial. We have not found a system that specifically labels mtDNA for subsequent tracing inside EVs or for encapsulation within artificial EVs (which falls outside our expertise). Therefore, we employed labeled mtDNA that we could trace after the embryos' internalization.

While we acknowledge that this approach is not perfect, it does demonstrate the internalization of mtDNA sequences within the embryo. We have revised the manuscript to eliminate any potential sources of confusion. If the reviewer or editors still have concerns about the experiment's suitability, we are open to removing it from the final version of the manuscript. Please refer to page 9 and lines 234-238 for more details."

Author Response

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

General comments:

To reviewer 1 and 3: The following sentences below were added at the beginning of the result section to clarify that the Gr gene expression analysis was performed using bimodal expression systems and to provide a reference that these expression profiles can generally be expected to represent endogenous Gr expression.

"Note that this and all previous Gr expression studies were performed using bimodal expression systems, mostly GAL4/UAS, whereby Gr promotors driving GAL4 are assumed to faithfully reproduce expression of the respective Gr genes. Importantly, we analyzed two or more Gr28-GAL4 insertion lines for each transgene, and at least two generated the same expression profiles (Mishra et al., 2018; Thorne and Amrein, 2008) providing evidence that the drivers reflect a fairly accurate expression profile of respective endogenous genes."

Specific comments:

Reviewer #1 (Recommendations For The Authors):

The important chemogenetic behavioral data would benefit from a clearer presentation including a cartoon to explain what the behavior is and how it is scored. Figure 2 is the key figure in this paper and it would be helpful if the figure were reorganized to guide the non-expert reader to the key result. I recommend labeling the positive controls Gr43a as "sweet" and Gr66a as "bitter" and perhaps organize the presentation to have the negative control at the left, then Gr28ba that had no effect, then group Gr28a with Gr43a for positive valence and Gr28bc with Gr66a for negative valence. I'm not sure what the value is of showing both 0.1 mM and 0.5 mM capsaicin, the text does not explain. The experiment in Figure 2B is important but non-experts will not understand what is being done here - can the authors please provide a cartoon like those in Figure 1 showing what cells are being subjected to chemogenetics and how this differs from Figure 2A?

The reviewer is correct that much can be improved, which we hope to have accomplished with the modifications in Figure 2. We re-organized it to deliver the key result to non-expert readers in an easy way. We added cartoons both explaining how the two-choice preference assays were conducted and indicating which cells express UAS-VR1. The cartoon in Figure 1E and Figure 2A are now directly relatable and should clarify what cells express VR1 (in Figure 2). Positive and negative control experiments using Gr43aGAL4 (a GAL4 knock-in; Miyamoto et al., 2013) and Gr66a-GAL4 are highlighted in the Figure and mentioned upfront in the text to make clear to what the experimental larvae can be compared. We also excluded larvae responses to 0.5 mM capsaicin.

1. The AlphaFold ligand docking in Figure 8 is conducted with Gr28bc monomers, which are unlikely to be the in vivo relevant structure, given that the related OR/ORCO ancestor structures are tetramers. I recommend that this component of the paper either be removed entirely or that the authors redo the in silico work using the AlphaFold-Multimer package reported by Hassabis and Jumper in 2022 https://www.biorxiv.org/content/10.1101/2021.10.04.463034v2. It will be interesting to see what a tetramer structure looks like with the ligand.

We tried but were able to use the recommended package. Even if it were, the problem is that we do not know the partner of Gr28b.c. And while it is not clear whether and how extensive changes in the ligand binding pockets occur when using the monomer prediciton vs a multimer package, we followed the reviewer’s suggestion and removed the modeling from the manuscript.

Minor points:

1. Line 80: I do not think it is biophysically or biochemically plausible that GRs and IRs would assemble into functional heteromeric channels and suggest that the authors either explain how that would work or remove this speculative comment.

We have removed this sentence.

1. Line 246-248: I would tone down the speculation about GR subunit composition - it's still too early days to understand the stoichiometry or the extent that any of the broadly expressed GRs is a co-receptor.

We did not indulge in the possible stoichiometry of Gr complexes, but merely mention that they are composed in general of two or more Gr subunits, for which clear genetic evidence exists: Up to three different putative bitter Gr genes are necessary to elicit responses to bitter compounds, and at least two putative sugar Gr genes are necessary to restore behavioral responses to any sweet tasting chemicals (sugars). Regardless, we have toned down the language, stating now:

“Given the multimeric nature of bitter taste receptors (Sung et al., 2017), one possibility is that the absence of a Gr subunit not required for the detection of denatonium (Gr66a) could favor formation of multimeric complexes containing Gr subunits that recognize this compound (Gr28b.a and/or Gr28b.c).”

1. Line 284: I don't think that co-expression necessarily means that GRs form heteromultimeric channels. It's equally possible that the cell controls subunit assembly to avoid mixing and matching ligand-selective subunits at will. I would tone this down - it's still speculative at this stage. We don't even know yet how this works for OR-Orco, where we do have structures. There is not yet an OR-Orco Cryo-EM structure, so we do not know what the subunit stoichiometry is.

We are not sure what the reviewer’s concern is. While direct biochemical or biophysical evidence is currently lacking, there is strong genetic evidence for heteromeric composition of Gr complexes, both from studies of bitter and sweet receptors/neurons (see response above). It is likely that intrinsic properties facilitate assembly of certain Grs within a taste receptor complex. We have refrained from any speculation about stoichiometry, though given the relatedness of Grs and Ors, it would not be far-fetched to propose that taste receptor complexes are also tetrameric in nature, which was recently proposed for a homomeric channel of the bombyx mori homolog of Gr43a, BmGr9 (Morinaga et al., 2022).

1. Line 305: the work of Emily Troemel and Cori Bargmann PMID: 9346234 should be cited in the Discussion. Theirs was the first experiment to show that valence was a feature of the neuron and not the receptor(s) it expresses.

We have now cited this work in the discussion to acknowledge this important discovery.

1. Figure 1 - the clarity of the organization of the figure could be improved for non-experts. For instance, can the key for the abbreviations be written out at the right of Figure 1A? Second, it is confusing to talk about DOG/TOG neurons "projecting" to the DO/TO - I think the authors mean dendritic innervation, not axons projecting. Maybe having a diagram that cartoons a closeup of the DOG/TOG neurons and how they innervate the cuticular structures would make this clearer. I struggled to go from the pretty staining at the left of B and C to the schematics at the right that colored in which neurons express which receptors.

We appreciate these comments regarding clarity and have amended Figure 1 and made necessary changes in the text and the Figure legend.

1. Figure 3 would benefit from a summary cartoon relating back to the cartoons in Figure 1 to summarize what neurons the authors think are necessary for bitter avoidance.

We very much appreciate this suggestion and have increased clarity by referring to the carton in Figures 1 and 2.

1. Figure 4B - the lowercase letters indicating Gr28 subunits that are being expressed under UAS control (bottom row of table "UAS-Gr28") are easily confused for the lowercase letters a, b used throughout to signify significant differences. I recommend that the authors write out the gene names in this figure to clarify the genes in the rescue experiment.

We changed the text in the Figure accordingly.

1. For non-experts it would be helpful to have a map of the Gr28 gene locus so that people understand the arrangement of the genes and how the Gal4 driver lines map onto the locus.

We have now included such a map in Figure 1B.

Reviewer #2 (Recommendations For The Authors):

1. In the title and multiple times in the text (e.g. lines 121-122), the authors make the claim that different Gr28 genes mediate opposing behaviors. At first, I was not convinced of this claim, but I now believe it may be warranted if integrating the present results with results from Mishra et al., 2018. In the present study, the authors show that different neurons drive opposing behaviors, but they did not show that the genes themselves mediate opposing behaviors. They show evidence for the role of Gr28bc and Gr28ba in aversion, but not the role of Gr28a in attraction. I was thinking that there could be other receptors in Gr28a-expressing neurons that mediate attraction. However, Mishra et al. showed that mutation of all Gr28 genes abolishes preference for RNA/ribose as well as detection of these compounds by Gr28a+ neurons of the terminal organ, an impairment that could be rescued by expressing Gr28a (although Gr28b genes seem to have similar functions), and the present study shows that the other Gr28 genes are not co-expressed with Gr28a in the terminal organ. Is this the line of reasoning that we must take to come to the conclusion in the title? If so, I don't believe it comes through clearly in the paper.

We appreciate this observation. We have modified language in the abstract and the introduction to reflect previous reports of Gr28a as an RNA/ribose receptor (Mishra et al., 2018) and its conversation across dipteran insects (Fujii et al., 2023) where we showed that appetitive behavior for RNA can be mediated via the mosquito homologs in transgenic Drosophila larvae. The reviewer is correct in that there are other appetitive neurons, namely those expressing Gr43a, which defines a set distinct from and non-overlapping with Gr28a neurons (Mishra 2018). This additional information is included in the Figure 1, summarizing expression of the Gr28 genes, Gr66a and Gr43a.

1. The Figure 6 schematic does not show Gr66a+ Gr28- cells as being connected to avoidance behavior. This seems misleading because it seems likely that these cells do promote avoidance (based on known functions of other Gr66a cells). Also, it is not clear what the red dashed line represents.

The Gr66a neurons are indeed also avoidance mediating, but it is not clear which subgroup of these neurons is necessary. Our analysis in Figure 2 using Gr28b.c driving Kir2.1 suggests that a small subset of Gr66a neurons is sufficient to mediate avoidance. It is, however, possible that other subsets not including Gr28b.c can also mediate avoidance. The figure has been modified accordingly, as has the model in Figure 7.

1. I would suggest including the description of Figures 7-8 in the Results instead of the Discussion. In Figure 8, it would be helpful to superimpose labels for the transmembrane domains and extracellular/intracellular sides to better interpret the models.

The modeling was removed from the manuscript (see response above to reviewer 1).

1. The finding that Gr66a mutants show increased denatonium and quinine avoidance (Figure 4 - figure supplement 1) seems like a non sequitur, as it does not relate to the analysis of Gr28 genes. I support the inclusion of these interesting results, but perhaps it could be stated why this experiment was conducted (e.g. as a positive control).

We have reworded this section to make clear why Gr66a mutants were tested (possibly being part of a denatonium receptor complex).

1. An introduction to the nomenclature and gene structure for the Gr28 genes would be helpful. It's not clear how they're all related, e.g. that the Gr28b genes share some exons whereas Gr28a is separate. The Results section alludes to "the high level of similarity between these receptors", and some sort of reference or quantification for this statement would be useful. I also think naming the Gr28b genes with a period (e.g. "Gr28b.c") may be more consistent with the literature.

We have added the structure of the Gr28 genes in the Figure 1B, which was also a suggestion by reviewer 1, and we have amended the naming of the genes.

1. Lines 79-80 state "some GRNs express members of both families", but no citation is provided.

As this sentence was deleted, based on a comment by reviewer 1, this point becomes mute.

1. There are several typos or grammatical mistakes that the authors may wish to correct (e.g. lines 73, 75, 91, 232, 334, 780, 788).

We appreciate the reviewer pointing these errors out to us. The mistakes were corrected.

Reviewer #3 (Recommendations For The Authors):

• Silencing experiments suggest a role for Gr28bc in the avoidance of quinine (Figure 3), while imaging experiments do not support this role (Figure 5G). An explanation is needed to reconcile these findings.

The imaging experiments do support a role for Gr28b proteins in quinine detection in the specific TOG GRN used for all live imaging (Figure 5). This GRN in DGr28 larvae has a significantly lower Ca2+ responses to quinine compared to controls. However, the Ca2+ response could not be rescued to wild type levels by supplementing single Gr28b subunits, suggesting multiple Gr28b proteins are present in a quinine specific receptor complex in this GRN. Also note that Ca2+ responses of DGr28 larvae to quinine is not completely abolished, suggesting some redundancy, possible via Gr33a (Apostolopoulou et al., 2014), also supported by DGr28 larvae, which have still a robust avoidance to quinine. We are confident we have been clearer in arguing this point, both the result and especially the discussion section.

• Silencing experiments specifically targeted neurons expressing Gr28bc and Gr28be (Figure 3). It is important to note why other neurons expressing different members of the Gr28 family were not included in this analysis.

• Inconsistency is observed in the use of different reagents across the experiments. Specifically, all six Gal4 lines were utilized in the Chemical Activation experiments, while only two lines were employed in the silencing experiments.

The silencing experiments asked the specific questions as to what neurons are necessary for avoidance of bitter chemicals. Gr28a-GAL4 and Gr28b.a-GAL4 neurons were omitted because the former mediate feeding preference and not avoidance, and the latter is expressed in the same neurons as Gr28b.e (Figure 1). The remaining two Gr28b genes, Gr28b.b-GAL4 and Gr28b.d-GAL4 are not expressed in the larval taste system (Mishra et al., 2018) as we stated in the introduction/result section, and they were therefore not included in the chemogenetic or Kir2.1 inactivation experiments. We included these genes in rescue experiments, simply to test whether or not they can restore function for sensing denatonium.

As for the chemogenetic activation experiments: two of the GAL4 lines are controls (Gr66a-GAL4 and Gr43GAL4), that were needed to show what can be expected from these experiments.

• The authors did not acknowledge that neurons expressing members of the GR28 family also express other Gr family members, which could potentially contribute to the detection and behavioral responses to the tested bitter compounds.

We believe we did, but we have made that much more explicit in the revised manuscript.

• Gal4 lines from various studies exhibit varying expression patterns, highlighting the necessity for improved reagents. These findings also suggest the importance of employing different Gal4 lines for each receptor to validate the results of the current study.

See response at the beginning of our rebuttal.

• Activating or silencing neurons pertains to the function of the neurons rather than the receptors.

We agree and nothing in the manuscript states otherwise.

Reviewer #2 (Public Review):

Summary:

This manuscript describes P. falciparum population structure in Zanzibar and mainland Tanzania. 282 samples were typed using molecular inversion probes. The manuscript is overall well-written and shows a clear population structure. It follows a similar manuscript published earlier this year, which typed a similar number of samples collected mostly in the same sites around the same time. The current manuscript extends this work by including a large number of samples from coastal Tanzania, and by including clinical samples, allowing for a comparison with asymptomatic samples.

The two studies made overall very similar findings, including strong small-scale population structure, related infections on Zanzibar and the mainland, near-clonal expansion on Pemba, and frequency of markers of drug resistance. Despite these similarities, the previous study is mentioned a single time in the discussion (in contrast, the previous research from the authors of the current study is more thoroughly discussed). The authors missed an opportunity here to highlight the similar findings of the two studies.

Strengths:

The overall results show a clear pattern of population structure. The finding of highly related infections detected in close proximity shows local transmission and can possibly be leveraged for targeted control.

Weaknesses:

A number of points need clarification:

It is overall quite challenging to keep track of the number of samples analyzed. I believe the number of samples used to study population structure was 282 (line 141), thus this number should be included in the abstract rather than 391. It is unclear where the number 232 on line 205 comes from, I failed to deduct this number from supplementary table 1.

Also, Table 1 and Supplementary Table 1 should be swapped. It is more important for the reader to know the number of samples included in the analysis (as given in Supplementary Table 1) than the number collected. Possibly, the two tables could be combined in a clever way.

Methods<br /> The authors took the somewhat unusual decision to apply K-means clustering to GPS coordinates to determine how to combine their data into a cluster. There is an obvious cluster on Pemba islands and three clusters on Unguja. Based on the map, I assume that one of these three clusters is mostly urban, while the other two are more rural. It would be helpful to have a bit more information about that in the methods. See also comments on maps in Figures 1 and 2 below.

Following this point, in Supplemental Figure 5 I fail to see an inflection point at K=4. If there is one, it will be so weak that it is hardly informative. I think selecting 4 clusters in Zanzibar is fine, but the justification based on this figure is unclear.

For the drug resistance loci, it is stated that "we further removed SNPs with less than 0.005 population frequency." Was the denominator for this analysis the entire population, or were Zanzibar and mainland samples assessed separately? If the latter, as for all markers <200 samples were typed per site, there could not be a meaningful way of applying this threshold. Given data were available for 200-300 samples for each marker, does this simply mean that each SNP needed to be present twice?

Discussion:<br /> I was a bit surprised to read the following statement, given Zanzibar is one of the few places that has an effective reactive case detection program in place: "Thus, directly targeting local malaria transmission, including the asymptomatic reservoir which contributes to sustained transmission (Barry et al., 2021; Sumner et al., 2021), may be an important focus for ultimately achieving malaria control in the archipelago (Björkman & Morris, 2020)." I think the current RACD program should be mentioned and referenced. A number of studies have investigated this program.

The discussion states that "In Zanzibar, we see this both within and between shehias, suggesting that parasite gene flow occurs over both short and long distances." I think the term 'long distances' should be better defined. Figure 4 shows that highly related infections rarely span beyond 20-30 km. In many epidemiological studies, this would still be considered short distances.

Lines 330-331: "Polymorphisms associated with artemisinin resistance did not appear in this population." Do you refer to background mutations here? Otherwise, the sentence seems to repeat lines 324. Please clarify.

Line 344: The opinion paper by Bousema et al. in 2012 was followed by a field trial in Kenya (Bousema et al, 2016) that found that targeting hotspots did NOT have an impact beyond the actual hotspot. This (and other) more recent finding needs to be considered when arguing for hotspot-targeted interventions in Zanzibar.

Figures and Tables:<br /> Table 2: Why not enter '0' if a mutation was not detected? 'ND' is somewhat confusing, as the prevalence is indeed 0%.

Figure 1: Panel A is very hard to read. I don't think there is a meaningful way to display a 3D-panel in 2D. Two panels showing PC1 vs. PC2 and PC1 vs. PC3 would be better. I also believe the legend 'PC2' is placed in the wrong position (along the Y-axis of panel 2).

Supplementary Figure 2B suffers from the same issue.

The maps for Figures 1 and 2 don't correspond. Assuming Kati represents cluster 4 in Figure 2, the name is put in the wrong position. If the grouping of shehias is different between the Figures, please add an explanation of why this is.

Figure 2: In the main panel, please clarify what the lines indicate (median and quartiles?). It is very difficult to see anything except the outliers. I wonder whether another way of displaying these data would be clearer. Maybe a table with medians and confidence intervals would be better (or that data could be added to the plots). The current plots might be misleading as they are dominated by outliers.

In the insert, the cluster number should not only be given as a color code but also added to the map. The current version will be impossible to read for people with color vision impairment, and it is confusing for any reader as the numbers don't appear to follow any logic (e.g. north to south).

The legend for Figure 3 is difficult to follow. I do not understand what the difference in binning was in panels A and B compared to C.

Font sizes for panel C differ, and it is not aligned with the other panels.

Why is Kusini included in Supplemental Figure 4, but not in Figure 1?

Supplemental Figures 6 and 7: What does the width of the line indicate?

What was the motivation not to put these lines on the map, as in Figure 4A? This might make it easier to interpret the data.

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Reply to the reviewers

Reviewer #1:

Comment: The author investigated the role of the stress sensor pathway in the mechanism of tumor cell survival<br /> They identified a long noncoding RNA as JUNI that regulates antagonizing MAP phosphatase and favors the JUN transcription. JUNI correlated with the survival of several cancer histotypes, particularly in RCC, as a highly specific and correlated prognosis.

The abstract although not always required from the journal should be divided into methods used to reach the main findings and clear presentation of results

Response: We do not know yet to which Journal the paper will be sent. The format will be adjusted to the Journal requirements.

it is unclear whether JUNI is a positive or negative regulator of JUI (I assume the reviewer meant JUN)

Response: The text in the abstract was changed to” JUNI positively regulates the expression of its neighboring gene JUN, a key transducer of signals that regulate multiple transcriptional outputs.”

Hope it is clearer now

When the author indicates that JUNI antagonizes MAP PHOSPHATASE is not correct the term antagonism is related to receptors but the authors did not show any receptor.

Response: The term "antagonism" does not only refer to receptor drugs. In pharmacology, antagonism generally describes the interaction between a drug (or other molecule) and a receptor or biological target that results in the inhibition or blocking of the receptor's activity. However, this concept can extend beyond receptor drugs and apply to various biological interactions.

Outside of the realm of drugs and receptors, antagonism can also refer to antagonistic relationships between different biological processes, molecules, or organisms.

Overall, while antagonism is commonly discussed in the context of receptor drugs, the concept of antagonism can apply to a broader range of interactions in biology and other fields.

Response: The p values for the prognostic values of JUNI and DUSP14 in RCC were added to the abstract.

Generally, Jun oncogene correlated with poor overall survival while the table indicates promote survival so good prognosis?

Response: This manuscript describes for the first time the biological activity and cancer relevance of JUNI. It positively regulates stress induced c-Jun and can be used as prognostic marker in ccRCC.

The significance of JUNI and its interactome in ccRCC prognosis is unequivocal, according to data analysis of cancer relevant data (TCGA) regardless to its effects on c-Jun. The concern raised by reviewer 1 and 2 is whether the cancer-relevant effects are mediated by c-Jun regulation. We suggest that despite regulating stress induced c-Jun, they are not! This suggestion is based on three points: 1. We show in the manuscript that a large portion of JUNI dependent effects on cellular survival activity is c-Jun independent. 2. We describe many interacting proteins that may, in a JUN-independent manner, affect tumorigenesis. 3. In this study we examined JUNI’s functions which are cell-autonomous. However, neither the non -autonomous effects nor effects on cells that compose the tumor environment were studied. Reports that lncRNAs may have a role in immune responses and high expression of JUNI in CD8 cells may suggest this direction for future investigation (Carpenter, S et al. science, 341(6147), pp.789-792; Mickaël, M. et al https://doi.org/10.1101/2021.12.01.470587)

Therefore, we assume that direct correlations in every biological activity between JUNI and JUN is an over simplified consumption. Analogy for that can be found with another major regulator of c-Jun, JNK, which is stress induced, c-Jun regulator involved in stress-induced cell death, whereas c-Jun itself is contributing in many cases to drug resistance.

The introduction contains the main information to follow the role of JUN and renal carcinoma<br /> However, should be improved with background on the key role of stress genes in the pro-survival pathway of tumors during progression and hypoxia condition. Too many references on long noncoding compared to the JUN complex with AP-1 and transformation

Response: A section describing the major stress pathway in ccRCC, HIF 1 and its role in ccrCC was added. Due to the limitation of word count in most journals we cannot expend this section further

Results In Figure 1 the authors showed expression levels of JUNI and JUN that are clearly different after UV stimuli. they demonstrate that are both regulated by UV but the amount and the time are different. the author should comment on these data if they want to study the regulative mechanism

Response: The following comment was added at the end of the first section: Overall, these results suggested that JUNI is a stress-induced gene whose expression pattern resembles that of JUN, therefore, we investigated the potential existence of regulatory effects between the two genes, especially post exposure of cells to stress.

Figure 1 F the cellular distribution of JUNI which is the rational of this experiment to provide that is into nucleus while normally is into the cytoplasm? What adds this experiment?

Response: This is the first reported description of JUNI. We attempted to characterize it as much as possible. It’s localization was not described previously and we suggest that it is mainly nuclear. A novel important information that should be presented.

In Figure 2 the authors provided that the kinase pathway is important for Jun regulation but the effect on JUNI a Luciferase assay needs to be provided

Response: We respectfully disagree with the reviewer. We believe that examining the expression from a DNA fragment identical to the endogenous one is superior to artificial system, such as luciferase.

In Figure 3 for Migration assay is necessary to see cells on the other side of the filter by staining not a graphical representation

Response: The graphical representation is an accumulated result of at least 3 experiment. However, a figure representing a single experiment was added as a supplement figure s1.

The experiment on kinase does not add any data to what is already known on jun probably should be shifted in Figure 6

Response: We apologize, this question was not fully understood as there is no experiment on kinase in figure 3. If case the reviewer was referring to kinase inhibition in Fig 2A we do think it is needed as a positive control for the kinases activity.

Table 1 is cited two times once in the context of Figure 3 and then in Figure 6 indicating that the authors go forward and back on their experimental design

Response: Table 1 is indeed referred to in two places. It is first mentioned when we investigated the potential relevance of JUNI for human cancer, given its regulatory impact on the neighboring JUN gene and its influence on motility. Later, the types of cancers described in figure 1 were further processed in order to examine relations between JUNI and DUSP14 in human cancer. We do not see it as a flaw in experimental design but rather as further evolution of the story based on data discovered in earlier stages.

in figure 4 the apoptotic cells are not clearly visible a specific staining marker is necessary to provide the phenomenon

Response: Two corrections were made to demonstrate apoptosis clearly. The pictures in Figure 4 panel A were replaced with a better-quality image with addition of DNA staining to demonstrate the cell death clearer, appearance of cell blebbing and nuclear fragmentation. Panel B demonstrating increase in cleaved caspase 3 in JUNI silenced cells after all treatment was added.

Additionally XTT assay should be reported as the percentage of survival cells not staining incorporated compared to untreated cells over time

Response: We do apologize for the legend omission, but XTT assays, colonies formation and soft agar colonies formation are presented in Figure 4 H-J and Figure S3 for all cell lines

The data on prognosis and correlation of gene expression are not clearly presented and discussed

Response: Figure S4 was replaced by table S3 to demonstrate clearer the differences in Medians survival caused by JUNI of DUSP 14. Text was changed in the last section of results.

The western blot need to be quantified

Response: All blots were quantified

Reviewer #2:

1. While the experimental data showed JUNI, like c-JUN, is pro-survival of cancer cells, the clinical sample analyses correlated it positively with patients' survival. This discrepancy casts doubts in significance of the findings. The authors need to re-evaluate their data and conclusion

Response: This manuscript describes for the first time the biological activity and cancer relevance of JUNI. It positively regulates stress induced c-Jun and can be used as prognostic marker in ccRCC.

The significance of JUNI and its interactome in ccRCC prognosis is unequivocal, according to data analysis of cancer relevant data (TCGA) regardless to its effects on c-Jun. The concern raised by reviewer 1 and 2 is whether the cancer-relevant effects are mediated by c-Jun regulation. We suggest that despite regulating stress induced c-Jun, they are not! This suggestion is based on three points: 1. We show in the manuscript that a large portion of JUNI dependent effects on cellular survival activity is c-Jun independent. 2. We describe many interacting proteins that may, in a JUN-independent manner, affect tumorigenesis. 3. In this study we examined JUNI’s functions which are cell-autonomous. However, neither the non -autonomous effects nor effects on cells that compose the tumor environment were studied. Reports that lncRNAs may have a role in immune responses and high expression of JUNI in CD8 cells may suggest this direction for future investigation (Carpenter, S et al. science, 341(6147), pp.789-792; Mickaël, M. et al https://doi.org/10.1101/2021.12.01.470587)

Therefore, we assume that direct correlations in every biological activity between JUNI and JUN is an over simplified consumption. Analogy for that can be found with another major regulator of c-Jun, JNK, which is stress induced, c-Jun regulator involved in stress-induced cell death, whereas c-Jun itself is contributing in many cases to drug resistance.

Response: The Western blotting data need at least triplicate biological experiments and quantification. This is particularly important for trivial differences, such as shown in Fig. 6.

Response: All westerns X=3. Representative experiments are depicted. Quantification was added.

The identification and gene structure of LINC01135 and its relevance to c-Jun need better clarity

Response: First result section. “According to ENCODE data, JUNI contains five main exons and has multiple isoforms. Twenty-seven different transcript isoforms were described according to LNCipedia ranging from 213 to 6213 bases {Volders, 2019 #2907}. The relevance to c-Jun was referred to in discussion: Both the effects of JUNI on c-Jun induction and cellular survival were demonstrated using under-expression conditions by targeting, the common, first, exon of JUNI. Nevertheless, this exon was also sufficient for c-Jun induction upon stress exposure, under conditions of overexpression.

Page 9-10, Line 198-199, there are no results in Fig. 1 showing that JUNI induction was dependent to serum stimulation of starved cells

Response: “ Similar to JUN, the induction was dose dependent (Fig 1C), and the rapid response to stress (Fig 1D) as well as to serum stimulation of starved cells, identified by others (36), qualifies it as an “immediate early” lncRNA.”

Serum stimulation is described in reference 36

What is the Y-axis in figures 2B, 4E-G

Response: Legend was added to Y-axis of Figures 2B and 4 E-G

In Fig. 3B, actin image is missing

Response: Actin was hidden in the graphic process. Corrected.

In Fig. 4. brightfield images are inaccurate for distinguishing apoptosis and necrosis. Additional molecular markers need to be used, such as caspase-3 cleavage and LDH release

Response: Two corrections were made to demonstrate apoptosis clearly. The pictures in Figure 4 panel A were replaced with a better-quality image with addition of DNA staining to demonstrate the cell death clearer, appearance of cell blebbing and nuclear fragmentation. Panel B demonstrating increase in cleaved caspase 3 in JUNI silenced cells after all treatment was added.

The inconsistency of using four cell types in each assay. For example, in Fig. 4A, B, E-G and Suppl Fig. 1, HMCB, MDA-MB-231 and CHL1 cells were used to test the short-term effect of JUNI knockdown on cell survival, whereas Hela, MDA-MB-231 and CHL1 cells were chosen to determine the long-term effect of JUNI knockdown. Similar case in other figures.

Response: Effects on Jun regulation and the effects on long term survival were tested in all four cell lines both by XTT and clonogenic assays whereas effects on short term survival were tested in three out of the four cell lines. It is practically impossible to perform a study of this magnitude were all assays were tested in all cell lines. Using four cell lines was applied to prove the major points.

In Fig. 5D, no difference of c-Jun expression between NS and siJUN groups

Response: Correct, the western in 5D was replaced by a more representative one

Cell survival in Fig. 5 lacked statistical analyses

Response: Error bars were mistakably omitted. The figure was corrected.

In Suppl Fig. 2C, there is no figure to show the reduced colonies formation in soft agar in MDA-MB-231 cells, contradicting to that stated in the manuscript

Response: Indeed Figure 4 J and S3 C presented colonies formation in HMCB and HeLa cells. The text was corrected.

Reviewer #3: "linc01135" - this is a human gene, should be capitalized

Response: linc01135 was capitalized

Please indicate primers in Fig1A and mention this in relevant part of Results

Response: The following section was added: “Importantly, ENCODE predicts that the first exon is shared by all, therefore, all primers to analyze JUNI’s expression as well as siRNAs to silence it, were targeted for this exon.”

Fig1C-F - please add a legend to explain the colors

Response: Legend was added into the Figure as well

Copy number: It is important to establish the approximate copy number of JUNI RNAs in the cell lines tested. FISH would be one appropriate method. This could also be referenced back to the RNA-seq TPM values. Are we talking about <1 copy /cell, or many? Quick inspection of ENCODE RNA-seq in the UCSC browser suggest an intermediate value that varies between cell lines. This value is very important when interpreting mechanistic experiments later on

Response: The copy number in HMCB and MDA-MB-231 was calculated by comparison of CT values obtained from RNAs from a known number of cells relative to calibration curve of known concentrations of JUNI. The following section was added to the first paragraph of the results: “quantitation of JUNI’s copy number in untreated HMCB and MBA-MD-231 cells revealed the presence of minimal amount of about 8 copies per cell”

Fig3 - again, no figure legends, difficult for reader

Response: Legend was added to Fig. 3A

In general, the figures could be much more clearly annotated and presented with more care. They do not do justice to the quality of the work itself. For example, Fig4E-G why not label each panel with the time course, the cell line tested etc etc to save us the work of digging through the Legends?

Response: We thank the reviewer for this remark. All figures were corrected, legends and proteins quantification was added.

Rescue experiments: The rescue experiments in Fig5D are nicely done and the results are interesting. However, I would request the authors to perform similar experiments with JUNI rescue. Specifically, to knock down JUNI with siRNA, and then reintroduce it from an 'immune' expression plasmid, where the siRNA site is mutated. This will further strengthen the claim that JUNI siRNA is acting through the intended target to cause observed effects on cell viability

Response: As the effects on survival are strongest in the longer term, 14 days after silencing, rescue experiments were performed to test the rescue in the survival of HMCB and HeLa cells using clonogenic assays. Results are presented in figure 4 L

IncPrint data: was Jun protein found to be an interactor? This might be mentioned in the text, whether it is yes or no

Response: c-Jun was screened and did not interact with JUNI. The text was changed as following” Interestingly, c-Jun itself does not interact with JUNI (Table S2, Normalized luciferase intensity MS2, RLU =0.44). By contrast, the dual specificity protein phosphatase 14….”

Expression: A key issue is the expression of JUNI in healthy and diseased cells and organs. Is JUNI ubiquitous (and essential to both healthy and tumor cells), or is it specific to tumor cells? Which tumor types? This would be straightforward to find out from public data. I would suggest a main figure panel. Also, is JUNI upregulated across tumors? Could find this out from GEPIA2 or other databases.

Response: Figure 7E describing the levels of JUNI in variety of normal and tumor samples was added.

Non-tumor cells: Like many studies, this one focusses on effect of LOF in transformed cells. However, therapeutic relevance is tied to specific effect in transformed cells. Therefore I believe the paper would be vastly strengthened, if knockdowns+viability assays were also performed in some non-transformed cells. Eg HEK293, immortalised fibroblasts, RPE1 etc

Response: Indeed discrimination between Normal and cancer cells is an essential point for further research and translation. We examined the affects of silencing on spontaneously immortalized keratinocytes, HaCat cells, and the results are depicted in Figure 4 K.

Alternative reagents: The siRNA experiments are well performed with two independent sequences. An important additional experiment would be to replicate these experiments with antisense oligonucleotides. This would both further strengthen the confidence in experiments, and open more lines of potential therapies. This experiment I would consider optional

Response: Stable CRISPR can not be formed. We are currently constructing inducible CRISPR but the construction consumes longer time than the scope of this revision.

Advanced models: All the present experiments are performed in monolayer cell lines. The authors will no doubt be aware that the paper would be substantially strenghtened if functional experiments could be replicated in more advanced models: spheroids, PDX, explants, mice...

Response: We examined the protective role of JUNI in Doxorubicin treated spheroids of HMCB and CHL1 cells. The results are depicted in figure 4 D and E.

It may be just a prank for parents to take away their children's candy, but it can be devastating to a child's young mind and heart, and I don't think it's ethical for adults to use methods used to please adults to be applied to small children

Author Response

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

Thank you for the e-mail of 27th September that includes the eLife assessment and reviewers comments on manuscript eLife-RP-RA-2023-91861. We have considered these, added additional data and made various changes to the text as detailed below. We now submit a modified version that we would be happy to view as the ‘Version of Record’.

We are very pleased to note the highly positive reports from the reviewers. The major change we have made is to alter the Introduction to include further consideration of the development of the ‘bar-code’ hypothesis. As highlighted by reviewer 2 the Lefkowitz/Duke University Group have been major proponents of this concept. However, as with many topics their views did not emerge in isolation. Indeed we (specifically Tobin) were developing similar ideas in the same period (see Tobin et al., (2008) Trends Pharmacol Sci 29, 413-420). Moreover, other groups, particularly that of Clark and collaborators at University of Texas, were developing similar ideas using the beta2-adrenoceptor as a model at least as early as this (e.g. Tran et al., (2004) Mol Pharmacol 65, 196-206). As such we have re-written parts of the Introduction to reflect these early studies whilst retaining information on more recent studies that have greatly expanded such early work. This has resulted in the addition of extra references and re-numbering of the Reference section. We have also provided statistical analysis of agonist-induced arrestin interactions with the receptor as requested by a reviewer and performed additional studies to assess the effect of the GRK2/3 inhibitor in agonist-regulation of phosphorylation of the hFFA2-DREADD receptor. This has led to an additional author (Aisha M. Abdelmalik) being added to the paper.

To address first the ‘public reviews’

Reviewer 1

1. We agree that we do not at this point explore the implications of the tissue specific barcoding we observe and report. However, as noted by the reviewer these will be studies for the future.

2. The question of why these are only 2 widely expressed arrestins and very many GPCRs is not one we attempt to address here and groups using various arrestin ‘conformation’ sensors are probably much better placed to do so than we are.

Reviewer 2

1. It is difficult to address the potential low level of ‘background’ staining in some of the immunocytochemical images versus the ‘cleaner’ background in some of the immunoblotting images. The methods and techniques used are very distinct. However, it should be apparent that the immunoblotting studies are performed (both using cell lines and tissues) post-immunoprecipitation and this is likely to reduce such background to a minimum. This is obviously not the case in the immunocytochemical studies. It is also likely, even though the antisera are immune-selected against the peptide target, there may be some level of immune-recognition this is not limited to the phosphorylated residues.

2. Whilst this reviewer has commented in detail in the ‘recommendations’ section on the use of English, the other reviewers have not, and we do not find the manuscript challenging to follow or read.

Reviewer 3

1. We agree that the mass-spectrometry presented is not quantitative. The intention was for the mass spec to be a guide for the development of the antisera used in the study. We have re-written the initial part of the Results section (page 7) to state that phosphorylation of Ser297 was evident in the basal and agonist-stimulated receptor whilst phosphorylation of Ser296 was only evident following agonist addition.

2. Immunoblotting is intrinsically variable as parameters of antiserum titre in re-used samples is not assessed and although we are aware that FFA2 displays a degree of constitutive activity (see for example Hudson et al., (2012) J Biol Chem. 287(49):41195-209) we did not make any specific effort to supress this by, for example, including an inverse agonist ligand. Agonist-regulation of phosphorylation of the receptor, as detected in cell lines by the anti- pThr306/pThr310antiserum, is exceptionally clear cut in all the images displayed, and as we note for the pSer296/pSer297 antiserum this was always, in part, agonist-independent.

The point about compound 101 not being tested directly in the immunoblotting studies performed on the cell line-expressed receptor is a good one. We have now performed such studies which are shown as Figure 2E. These illustrate that the GRK2/3 inhibitor compound 101 does not reduce substantially agonist-induced phosphorylation of the receptor at least as detected by the pThr306/pThr310antiserum or by the pSer296/pSer297 antiserum. Equally this compound had little effect on recognition of the receptor. As the PD2 mutations which correspond to the targets for the pThr306/pThr310antiserum have no significant effect on recruitment of arrestin 3 in response to MOMBA (please see additional statistical analysis in modified Figure 2C) this is perhaps not surprising. Moreover, the PD1 mutations that correspond to the pSer296/pSer297antiserum also, in isolation, only have a partial effect of MOMBA-induced interactions with arrestin 3.

1. The use of phosphatase inhibitors is an integral part of these studies. As noted in Materials we used PhosSTOP (Roche, 4906837001). However, we failed to make it sufficiently clear that this reagent was present throughput sample preparation for both cell lines and tissue studies. This had been specified previously by two of us (SS, FN, see Fritzwanker S, Nagel F, Kliewer A, Stammer V, Schulz S. In situ visualization of opioid and cannabinoid drug effects using phosphosite-specific GPCR antibodies. Commun Biol. 6, 419 (2023)) but we agree this was insufficient and we now correct this oversight by making this explicit in Results.

Recommendations

Reviewer 1

Competing interest: We apologise for this typographic error. It is now corrected.

Figures: We have upgraded the figure images to 300dpi and this markedly improves readability

Reviewer 2

Revisiting writing: We thank the reviewer for their assessment of the text. However, we do not feel that ‘every sentence in the entire manuscript could be clarified’ is a reasonable statement. Neither of the other reviewers commented on this. Each of the authors read and approved the manuscript.

Figures: see response to Reviewer 1. We have greatly enhanced image quality at this part of the process.

Statistics on Figure 2: We apologise for this oversight. Although there were no significant differences in potency for MOMBA to promote interactions with arrestin-3 to each of the PD mutants versus wild type receptor, there were in terms of maximal effect. Statistical analysis was performed via one-way ANOVA followed by Dunnett’s multiple comparisons test. This is now detailed directly in Figure 2C and its associated legend. As noted by the reviewer there was indeed a highly significant effect of the GRK2/3 inhibitor compound 101 and this is now also noted in Figure 2D and its associated legend.

Units on page 9: pEC50 is considered as Molar by default but we have now specified this. PD1-4: It would be cumbersome to write out (and to read) 8 mutations that make up PD1-4 and hence we think this is specified appropriately in the Figure.

Reviewer 3

1. Mass spec: Please see comment point 1 to reviewer 3.

2. Immunoblotting and compound 101: We have done so.

3. Phosphatase inhibition: see public comments, reviewer 3.

Author Response

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

Reviewer #1 (Public Review):

The paper offers some potentially interesting insight into the allosteric communication pathways of the CTFR protein. A mutation to this protein can cause cystic fibrosis and both synthetic and endogenous ligands exert allosteric control of the function of this pivotal enzyme. The current study utilizes Gaussian Network Models (GNMs) of various substrate and mutational states of CFTR to quantify and characterize the role of individual residues in contributing to two main quantities that the authors deem important for allostery: transfer entropy (TE) and cross correlation. I found the TE of the Apo system and the corresponding statistical analysis particularly compelling. I found it difficult, however, to assess the limitations of the chosen model (GNM) and thus the degree of confidence I should have in the results. This mainly stems from a lack of a proposed mechanism by which allostery is achieved in the protein. Proposing a mechanism and presenting logical alternatives in the introduction would greatly benefit this manuscript. It would also allow the authors to place the allosteric mechanism of this protein in the broader context of protein allostery.

As detailed below, we went to great lengths to address these concerns, with an emphasis on the limitations of the model and a proposed mechanism. These revisions should hopefully warrant a re-evaluation of our manuscript.

Reviewer #1 (Recommendations For The Authors):

1. It would greatly benefit the paper to state a proposed mechanism by which allostery is achieved in this protein. Is this through ensemble selection, ensemble induction, or a purely dynamic mechanism? What is the rationale for choosing the proposed mechanism and what are reasonable alternative mechanisms? How does this mechanism fit in the broader context of protein allostery?

Following this comment, we added a VERY extensive description of the proposed mechanism by which allostery is achieved in CFTR and present the rationale for choosing this mechanism (lines 445-97 and Figure 7). Briefly, based on previous experimental results and our results we propose that no single model can explain allostery in CFTR, and that its allosteric mechanism is a combination of induced fit, ensemble selection, and a dynamic mechanism.

1. With a proposed mechanism in place, the choice of a GNM to investigate the mechanism and eliminate alternative mechanisms should be rationalized.

The rational for choosing GNM (and ANM-LD) to study the proposed mechanism is now given in lines 498-510. Please note however, that as mentioned in the response to point 1 (and detailed in lines 445-97), the choice of allosteric mechanism, and ruling out other alternatives was not based solely on GNM and ANM-LD, but also on previous experimental results.

1. A discussion of the strengths and limitations of the GNM are pivotal to understanding the limitations of the results shown. How sensitive are the results to specific details of the model(s)?

a. A discussion of the strengths and limitations of the GNM have been added to the introduction. Please see lines 107-122.

b. Sensitivity of the results to the specific details of GNM:

GNM uses two parameters: the force constant of harmonic interactions and the cutoff distance within which the existence of the interactions is considered. The force constant is uniform for all interactions and is taken as unity. Its value affects only the absolute values of the fluctuations (i.e., their scale) but not their distribution. As we are only looking at fluctuations in relative terms our results are insensitive to its value. GNM uses a cutoff distance of 7-10 Å in which interactions are considered (10 Å used in this study). To test the sensitivity of the results to the cutoff distance we repeated the calculations using 7 Å. As now discussed in lines 170-73 and shown in Figure S2 the results remained largely unchanged.

c. Sensitivity of the results to the specific details of TE: To identify cause-and-effect relations TE introduces a time delay (τ) between the movement of residues. The choice of τ is important: when τ is too small, only local cause-and-effect relations (between adjacent amino acids) will be revealed. if τ is too big, few (if any) cause-and-effect relations will manifest. This is analogous to the effects of a stone throne into a lake: look too soon, before the stone hits the water, and you’ll see no ripples. Look too late, the ripples will have already subsided. In a previous work (PMID 32320672), we studied in detail the effects of choosing different τ values and found that an optimal value of τ which maximizes the degree of collectivities of net TE values is in most cases 3× τopt (τopt is the time window in which the total TE of residues is maximized). Details of how τ was chosen were added to the methods section.

In general, the limitations of the chosen model(s) is difficult to determine from the current manuscript because it is devoid of details of the model. While I understand that GNMs have been widely used to study protein systems, the specifics of the model are central to the current work and thus should be provided somewhere in the manuscript.

a. As mentioned in our response above, the limitations of GNM are now presented (lines 107-122).

b. The specifics of the model are now given in more detail in the methods section.

c. In addition, as mentioned above, the results are largely independent of the values of the model’s parameters.

b. Would changing the force constants to a more anisotropic model qualitatively change the results?

a. GNM assumes isotropic fluctuations, and the calculations are based on this assumption. Therefore, GNM is inherently an isotropic model.

b. Importantly, we complement the GNM-TE calculations with ANM-LD simulations, which predict the normal modes in 3D using an anisotropic network model.

1. How repeatable is the difference between no ATP bound and ATP bound CFTR? I worry that the differences in TE in Figures 1 and 3A are mainly due to two different crystallization conditions. Is there evidence that two different structures of the same protein in the same ligand state lead to small changes in TE?

To address this concern, we repeated the calculations using the structures of the ATP-free and bound forms of zebrafish CFTR. As now explained in text (lines 298-303) and shown in Figure S8 the effects of ATP are highly repeatable.

1. Collective modes - why should we expect allostery to be in the most collective modes? Let alone the 10 most? Why not do a mode by mode analysis? Why, for example, were two modes removed page 9 first full paragraph?

a. Collective modes: We have erroneously referred to the slow modes as collective modes. This has now been corrected throughout the manuscript.

b. Let alone the 10 most?

c. why should we expect allostery to be in the most collective modes? Residues that are allosterically coupled are expected to display correlated motions. The slow modes (formerly referred to as “collective modes”) are generally the most collective ones, i.e., display the greatest degree of concerted motions. We therefore expect these modes to contain the allosteric information.

d. Furthermore, as now explained in the text (lines 163-69) and in Figure S1 the Eigenvalue decays of ATP-free and -bound CFTR demonstrate that the 10 slowest GNM modes sufficiently represent the entire dynamic spectrum (the distribution converges after the 10th slow mode).

e. Why not do a mode by mode analysis? It is entirely possible to do a mode-by-mode analysis. However, our view is that the allosteric dynamics of a protein is best represented by an ensemble of modes, rather than by individual ones. We found (as detailed here PMID 32320672) that it is more informative to first use the complete set of modes that encompasses the dynamics (the 10 slowest modes in our case) and then gradually remove the dominant modes.

f. As explained in text (lines 254-7) and more elaborately in our previous work (PMID 35644497), the large amplitude of the slowest modes may hide the presence of “faster” modes that may nevertheless be of functional importance. Removal of the 1-2 slowest modes often helps reveal such modes.

g. Why, for example, were two modes removed page 9 first full paragraph? As explained for the ATP-free form (lines 257-60), removal of these two slowest modes allowed the “surfacing” of dynamic features which were hidden before. We propose that these dynamic features are functionally relevant (see lines 304-19). Removal of other modes did not provide additional insight.

Minor issues:<br /> 1. Statements like "see shortly below" should be made more specific (or removed completely).

Corrected as suggested

1. "interfered" should be "inferred" page 10 middle of the first full paragraph

Corrected as suggested

1. End parenthesis after "(for an excellent explanation about the correlation between TE and allostery see (41)." Page 4 middle of first full paragraph

Corrected as suggested

Reviewer #2 (Public Review):

In this study, the authors used ANM-LD and GNM-based Transfer Entropy to investigate the allosteric communications network of CFTR. The modeling results are validated with experimental observations. Key residues were identified as pivotal allosteric sources and transducers and may account for disease mutations.

The paper is well written and the results are significant for understanding CFTR biology.

Reviewer #2 (Recommendations For The Authors):

Technical comments:

p4 Please explain how is the time delay parameter tau chosen (ie. three times the optimum tau value...)? It seems this unknown time should depend on the separation between i and j. Is the TE result sensitive to the choice of tau? How does the choice of cutoff distance of GNM affect the TE result?

a. The choice of τ is important: when τ is too small, only local cause-and-effect relations (between adjacent amino acids) will be revealed. if τ is too big, few (if any) cause-and-effect relations will manifest. This is analogous to the effects of a stone throne into a lake: look too soon, before the stone hits the water, and you’ll see no ripples. Look too late, the ripples will have already subsided. In a previous work (PMID 32320672), we studied in detail the effects of choosing different τ values and found that an optimal value of τ which maximizes the degree of collectivities of net TE values is in most cases 3× τopt (τopt is the time window in which the total TE of residues is maximized). Details of how τ was chosen were added to the methods section.

b. To test the sensitivity of the results to the cutoff distance we repeated the calculations using 7 Å. As now discussed in lines 170-173 and shown in Figure S2 the results remained largely unchanged.

It would be nice to directly validate the causal prediction by GNM-based TE. For example, is it in agreement with direct causal observation of MD simulation? If the dimer is too big for MD, perhaps MD is more feasible for the monomer (NBD1+TMD1).

a. The causality we determined using GNM-based TE is in good agreement with conclusions drawn from single channel electrophysiological recordings and rate-equilibrium free-energy relationship analysis (Sorum et al; Cell 2015, and see lines 8691, and 364-70).

b. To the best of our knowledge, causality relations in CFTR are yet to be determined by MD simulations (This is likely because the protein is too big and the conformational changes are very slow). We cannot therefore compare the causality.

c. Conducting MD simulations on half of CFTR (NBD1+TMD1) is not likely to be very informative: the ATP binding sites are formed at the interface of NBD1 and NBD2, and the ion translocation pathway at the interface of the TMDs.

p5 How are the TE peak positions different from other key positions as predicted by GNM, such as the hinge positions with minimal mobility of the dominant GNM modes?

Following this comment, we compared the positions of the GNM-TE peaks and the hinge positions as determined by GNM. As now discussed in lines 173-178 and shown in Figure S3 we observed partial overlap which was nevertheless statistically significant (Figure S3).

p7 How to select the 10 most collective GNM modes? Why not use the 10 slowest GNM modes?

We have actually used the 10 slowest GNM modes, but in an attempt to cater for the non-specialist reader, we referred to them as the most collective ones. This has now been corrected throughout the manuscript and the terminology that is now used is “10 slowest modes”

p9 There exist other ANM-based methods for conformational transition modeling. So it would be nice to discuss their similarity and differences from ANM-LD, and compare their predictions.

Alternative ANM (and other elastic network models) -based methods are now mentioned and referenced in lines 144-50. These methods are different from ANM-LD in the details of the all atom simulations and in their integration with the elastic network model. It is not trivial to reanalyze CFTR’s allostery using these methods and is beyond the scope of this work.

Regarding the prediction of order of residue motions, can one directly observe such order by superimposing some intermediate conformation of ANM-LD with the initial and end structure?

This would indeed be very attractive approach to visualize the order of events and following this comment we have tried to do just so. Unfortunately, we failed: Superimposing pairs of frames provided little insight, and we therefore compiled a video comprising all frames, or videos based on averages of several time delayed frames. We found that it is next to impossible to discern (using the naked eye) the directionality of the fluctuations and follow the order of conformational changes. Therefore, at this point, we have abandoned this endeavor.

Reviewer #3 (Public Review):

This study of CFTR, its mutants, dynamics, and effects of ATP binding, and drug binding is well written and highly informative. They have employed coarse-grained dynamics that help to interpret the dynamics in useful and highly informative ways. Overall the paper is highly informative and a pleasure to read.

The investigation of the effects of drugs is particularly interesting, but perhaps not fully formed.

This is a remarkably thorough computational investigation of the mechanics of CFTR, its mutants, and ATP binding and drug binding. It applies some novel appropriate methods to learn much about structure's allostery and the effects of drug bindings. It is, overall, an interesting and well written paper.

There are only two main questions I would like to ask about this quite thorough study.

Reviewer #3 (Recommendations For The Authors):

1. Is it possible that the relatively large exothermic ATP hydrolysis itself exerts a force that causes the observed transitions? Jernigan and others have explored this effect for GroEL and some other structures. The effects of ATP binding and hydrolysis are likely often confused, and both are likely to be important.

It is well established by many studies that ATP hydrolysis is not required to drive the conformational changes or to open the channel, and that ATP binding per-se is sufficient (e.g., We have clarified this point in lines 521-30.

1. For the case of ivacaftor, would a comparison of the motion's directions show that ivacaftor might be compensating simply by its mass being located in a site to compensate for the mass changes from the mutations (ENMs with masses needed to address this). We have observed such cases on opposite sides of a hinge.

We do not think that this is the case, from the following reasons:

a. Ivacaftor corrects many gating mutations (e.g., G551D, G178R, S549N, S549R, G551S, G970R, G1244E, S1251N, S1255P, G1349D) which are spread all over the protein. Ivacaftor binds to a single site in CFTR, and it is therefore unlikely that its mass contribution corrects all these diverse mass changes.

b. The residues that comprise the Ivacaftor binding were identified as allosteric “hotspots” in both the ATP-free and -bound forms (Figures 2B, 3B, and 6A), also in the absence of the drug. This indicates that the dynamic traits of this site is intrinsic to it, and that once bound, the drug acts by modulating these dynamics

The Abstract does not repeat some of the more interesting points made in the paper and would benefit from a substantial revision.

Corrected as suggested

There are just a few minor points (just words):

P 3 line 2 of first full ¶: "effects" should be "affects"

Corrected as suggested

P 6 first lilne "per-se" should be "per se"

Corrected as suggested

Further down that page "two set" should be "two sets"

Corrected as suggested

Even further down that same page "testimony" should be "support"

Corrected as suggested

P 10, 5 lines from the bottom "impose that" is awkward

Changed to “define”

Author Response

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

Response to Reviewers

To whom it may concern, Thank you for your constructive feedback on our manuscript. I appreciate the time and effort that you and the reviewers have dedicated to providing your valuable feedback. We are grateful to the reviewers for their insightful comments and suggestions for our paper. I have been able to incorporate changes to reflect the majority of these suggestions provided. I have updated the analysis scripts (at https://github.com/neurogenomics/reanalysis_Mathys_2019) and have listed these changes in blue below:

eLife assessment:

This work is useful as it highlights the importance of data analysis strategies in influencing outcomes during differential gene expression testing. While the manuscript has the potential to enhance awareness regarding data analysis choices in the community, its value could be further enhanced by providing a more comprehensive comparison of alternative methods and discussing the potential differences in preprocessing, such as scFLOW. The current analysis, although insightful, appears incomplete in addressing these aspects.

We thank the reviewing editors for this note. We agree that the differences in preprocessing will affect the results and conceal which step in our reanalysis resulted in the discrepancies we noted. To address this, we have split out our reanalysis into two separate parts - In the main body of the text we discuss the differences resulting from just changing the differential expression approach where we use the same processed data as the authors to enable a fair comparison. Secondly, we still provide the reprocessed data and perform differential expression analysis on it and discuss the cause and impact the differences in the processing steps made to the results.

Reviewer 1:

I think readers would be interested to learn more about the genes that were found "significant" by the original paper but sorted out by the authors. Did they just fall short of the cutoffs? If so, how many more samples would have been required to ascertain significance? This would yield a recommendation for future studies and an overall more positive/productive spirit to the manuscript. On the other hand, I suspect a fraction of DEGs were false positives due to differences in the proportions of cells from different individuals compared to the original analysis. Which percentage of DEGs does this apply to? Again, this would raise awareness of the issue and support the use of pseudobulk approaches.

To investigate the relationship between the genes and how they differ across our analysis we have added a correlation analysis between our different DE approaches (using the same processed data), see paragraph 5 in the manuscript and supplementary table 3. In short, we find that there is a high correlation in the genes’ fold change values across our pseudobulk analysis and the author’s pseudoreplication analysis on the same dataset (pearson R of 0.87 for an adjusted p-value of 0.05) which is somewhat expected given the DE approaches are applied to the same dataset. However, the p-values, which pertain to the likelihood that a gene’s expressional changes is related to the case/control differences in AD, and resulting DEGs vary considerably due to the artificially inflated confidence of the author’s approach (Fig. 1c-e). Despite there being a correlation between the pseudoreplciation and pseudobulk approaches here, we do not think it makes sense to consider how many more samples would have been required to ascertain significance. The differences in results between the two approaches is not negatable with sample size as many DEGs identified by pseudoreplication will be false positives as highlighted in previous work1,2,3,4. However, perhaps we are misinterpreting the reviewer, who may have meant a power analysis which we have not conducted. Such an undertaking would require analysing a multitude of snRNA-Seq of large sample sizes to garner a confident estimate for power calculations based on pseudobulk approaches. Although we agree with the reviewer that this would be beneficial to the field, we do not believe it is in scope for this work. On the reviewer’s note regarding a fraction of DEGs being false positives due to differences in the proportions of cells from different individuals compared to the original analysis - We have analysed the same processed data the authors used to negate the differences caused by the differing processing steps. We thank the reviewer for this suggestion. We also give more insight into the cause of these differences, namely on filtering our nuclei with large proportions of mitochondrial reads and discuss their effect in paragraph 3 (also see Supplementary Figure 2).

Given there are only a few DEGs, it would be good to show more data about these genes to allow better assessment of the robustness of the results, i.e., boxplots of the pseudobulk counts in the compared groups and perhaps heatmaps of the raw counts prior to aggregation. This could rule out concerns about outliers affecting the results.

In Supplementary Figure 3, we have added boxplots of the sum pseudobulked, trimmed mean of M-values (TMM) normalised counts for three of our identified DEGs (b) and three of the authors’ DEGs which they discuss in their manuscript (a) to show the differences in counts across AD pathology and controls for these genes. We hope this gives some insight into the transcriptional changes highlighted by the differing approaches. In our opinion, there is a clear difference in the transcriptional signal in the genes identified from pseudobulk which is not present for the genes identified from the authors approach.

Overall, I believe the paper would deliver a clearer message by mainlining the QC from the original study and only changing the DE analysis. However, if keeping the part about QC/batch correction:

• Assess to which degree changes in cell type proportion are indeed due to batch correction (as suggested in the text) and not filtering by looking at the annotated cell types in the original publication and those in your analysis.

• Also perform the analysis without changing QC and state the # of DEGs in both cases, to at least allow some disentanglement of the effect of different steps of the analysis.

• Please state the number of cells removed by each QC step in the supplementary note.

We thank the reviewer for this suggestion. We agree with performing the DE analysis on the same processed data as the original authors and have split out our reanalysis into two separate parts, primarily focussing on the discrepancies caused by the choice of differential expression (DE) approach. By splitting our analysis in this manner, we can identify the substantial differences in results caused by differing the DE approach in the study. Secondly, we can see how differences in preprocessing affects the DE results in isolation too – see paragraph 8 but in short, the fold change correlation between pseudobulk DE analyses on the reprocessed data vs authors processed data only had a moderate correlation (Pearson R of 0.57).

In regards to the number of cells removed by each QC step, we have added an aggregated view for all samples in supplementary table 3 and also give the full statistics per sample in our Github repository: https://github.com/neurogenomics/reanalysis_Mathys_2019. Moreover, we investigated the root cause in the differences in nuclei numbers, uncovering filtering down to mitochondrial read proportions as the main culprit (Supplementary Figure 2).

I recommend the authors read the following papers, assess whether their methodology agrees with them, and add citations as appropriate to support statements made in the manuscript.

We thank the reviewer for this comprehensive list. We have updated our manuscript and supplementary file and main text throughout to cite many of these where appropriate. We believe this helps add context to our decisions for the differing tools and approaches used as part of the processing pipeline with scFlow and the differential expression approach.

I believe the authors' intention was to show the results of their reanalysis not as a criticism of the original paper (which can hardly be faulted for their strategy which was state-of-the-art at the time and indeed they took extra measures attempting to ensure the reliability of their results), but primarily to raise awareness and provide recommendations for rigorous analysis of sc/snRNA-seq data for future studies.

We thank the reviewer for this note, this was exactly our intent. Furthermore, we are based in a dementia research institute and our aim is to ensure that ensure that the Alzheimer’s disease research field does not focus on spuriously identified genes.We have updated the text of the manuscript (start paragraph 2) to explicitly state this so our message is not misconstrued.

In my opinion, the purpose of the paper might be better served by focusing on the DE strategy without changing QC and instead detailing where/how DEGs were gained/lost and supporting whether these were false positives.

We agree that the differences in preprocessing will affect the results and conceal which step in our reanalysis resulted in the discrepancies we noted. To address this, we have split out our reanalysis into two separate parts - In the main body of the text we discuss the differences resulting from just changing the differential expression approach where we use the same processed data as the authors to enable a fair comparison. Secondly, we still provide the reprocessed data and perform differential expression analysis on it and discuss the impact the differences in the processing steps made to the results. As previously mentioned, we have also added further investigation into the DEGs identified, looking at the correlation across the differing approaches and plotting the counts for selected genes.

For instance, removal with a mitochondrial count of <5% seems harsh and might account for a large proportion of additional cells filtered out in comparison to the original analysis. There is no blanket "correct cutoff" for this percentage. For instance, the "classic" Seurat tutorial https://satijalab.org/seurat/articles/pbmc3k_tutorial.html uses the 5% threshold chosen by the authors, an MAD-based selection of cutoff arrived at 8% here https://www.sc-best-practices.org/preprocessing_visualization/quality_control.html, another "best practices" guide choses by default 10% https://bioconductor.org/books/3.17/OSCA.basic/quality-control.html#quality-control-discarded, etc. Generally, the % of mitochondrial reads varies a lot between datasets.

Apologies, the 5% cut-off was a misprint – the actual cut-off used was 10% which, as the reviewer notes, is on the higher side of what is recommended. We have updated our manuscript to rectify this mistake and discuss the differences in the number of cells caused by the two approaches to mitochondrial filtering in the manuscript (paragraph 3). We found that over 16,000 nuclei that were removed in our QC pipeline were kept by the author’s (Supplementary Fig. 2), explaining the discrepancy in the number of nuclei after QC. Based on Supplementary Fig. 2, it is clear the author’s approach was ineffective at removing nuclei with high proportions of mitochondrial reads which is indicative of cell death5,6. We hope this alleviates the reviewer’s concerns around our alternative processing approach. Moreover, as mentioned, we swapped to compare the differences by DE approaches on the same data to avoid any effect by this.

Reviewer 2:

The paper would be better if the authors merged this work with the scFLOW paper so that they can justify their analysis pipeline and show it in an influential dataset.

We thank the reviewer for this note. We would like to clarify that the purpose of our work was not to show the scFlow analysis pipeline on an influential dataset but rather to raise awareness and provide recommendations for rigorous analysis of single-cell and single-nucleus RNA-Seq data (sc/snRNA-Seq) for future studies and to help redirect the focus of the Alzheimer’s disease research field away from possible spuriously identified genes. We have updated our manuscript text to highlight this (see start paragraph 2). Furthermore, we are aware our original approach reprocessing the data with scFlow will affect the results and conceal which step in our reanalysis resulted in the discrepancies we noted. Thus, we have split out our reanalysis into two separate parts - In the main body of the text we discuss the differences resulting from just changing the differential expression approach where we use the same processed data as the authors to enable a fair comparison. Secondly, we still provide the reprocessed data so that the community can benefit from it and perform differential expression analysis on it and discuss the impact the differences in the processing steps made to the results. We have also added further references supporting the choice of steps and tools used in scFlow in the supplementary text which should address the reviewer’s concerns about justifying the analysis pipeline. Moreover, we identified the cause of the nuclei count differences caused by the two processing approaches, namely on filtering our nuclei with large proportions of mitochondrial reads and discuss their effect in paragraph 3 (also see Supplementary Figure 2).

A major contribution is the use of the authors' own inhouse pipeline for data preparation (scFLOW), but this software is unpublished since 2021 and consequently not yet refereed. It isn't reasonable to take this pipeline as being validated in the field.

We believe our answer to the previous point addresses these concerns - We have added references supporting the choice of steps and tools used in scFlow in the supplementary text which should address the reviewer’s concerns about justifying the analysis pipeline. Moreover, as a result of the pipeline we identified that 16,000 of the nuclei kept by the authors are likely of low quality and indicative of cell death with high mitochondrial read proportions5,6.

They also worry that the significant findings in Mathys' paper are influenced by the number of cells of each type. I'm sure it is since power is a function of sample size, but is this a bad thing? It seems odd that their approach is not influenced by sample size.

We thank the reviewer for highlighting this point. As they noted, we conclude that the original authors number of DEGs is just a product of the number of cells. However, the reviewer states that ‘It seems odd that their approach is not influenced by sample size’. An increase in the number of cells is not an increase in sample size since these cells are not independent from one another - they come from the same sample. Therefore, an increase in the number of cells should not result in an increase in the number of DEGs whereas an increase in the number of samples would. This point is the major issue with pseudoreplication approaches which over-estimate the confidence when performing differential expression due to the statistical dependence between cells from the same patient not being considered. See these references for more information on this point1,2,7,8. We have added a discussion of this point to our manuscript in paragraph 6.

Moreover, recent work has established that the genetic risk for Alzheimer’s disease acts primarily via microglia9,10. Thus, it would be reasonable to expect that the majority of large effect size DEGs identified would be found in this cell type. This is what we found with our pseudobulk differential expression approach – 96% of all DEGs were in microglia. We have updated the text of our manuscript (paragraph 5) to highlight this last point.

References 1. Murphy, A. E. & Skene, N. G. A balanced measure shows superior performance of pseudobulk methods in single-cell RNA-sequencing analysis. Nat. Commun. 13, 7851 (2022).

1. Squair, J. W. et al. Confronting false discoveries in single-cell differential expression. Nat. Commun. 12, 5692 (2021).

2. Crowell, H. L. et al. muscat detects subpopulation-specific state transitions from multi-sample multi-condition single-cell transcriptomics data. Nat. Commun. 11, 6077 (2020).

3. Soneson, C. & Robinson, M. D. Bias, robustness and scalability in single-cell differential expression analysis. Nat. Methods 15, 255–261 (2018).

4. Ilicic, T. et al. Classification of low quality cells from single-cell RNA-seq data. Genome Biol. 17, 29 (2016).

5. Heumos, L. et al. Best practices for single-cell analysis across modalities. Nat. Rev. Genet. 24, 550–572 (2023).

6. Zimmerman, K. D., Espeland, M. A. & Langefeld, C. D. A practical solution to pseudoreplication bias in single-cell studies. Nat. Commun. 12, 738 (2021).

7. Lazic, S. E. The problem of pseudoreplication in neuroscientific studies: is it affecting your analysis? BMC Neurosci. 11, 5 (2010).

8. Skene, N. G. & Grant, S. G. N. Identification of Vulnerable Cell Types in Major Brain Disorders Using Single Cell Transcriptomes and Expression Weighted Cell Type Enrichment. Front. Neurosci. 0, (2016).

9. McQuade, A. & Blurton-Jones, M. Microglia in Alzheimer’s disease: Exploring how genetics and phenotype influence risk. J. Mol. Biol. 431, 1805–1817 (2019).

Author Response

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

eLife assessment

The findings of this article provide valuable information on the changes of cell clusters induced by chronic periodontitis. The observation of a new fibroblast subpopulation, named AG fibroblasts, is interesting, and the strength of evidence presented is solid.

We thank the Reviewing Editor and the Senior Editor for the positive assessment and strong support for our study.

Public Reviews:

Reviewer #1 (Public Review):

In this article, the authors found a distinct fibroblast subpopulation named AG fibroblasts, which are capable of regulating myeloid cells, T cells and ILCs, and proposed that AG fibroblasts function as a previously unrecognized surveillant to orchestrate chronic gingival inflammation in periodontitis. Generally speaking, this article is innovative and interesting.

We truly appreciate this public review.

Reviewer #2 (Public Review):

This study proposed the AG fibroblast-neutrophil-ILC3 axis as a mechanism contributing to pathological inflammation in periodontitis. In this study single-cell transcriptomic analysis was performed. But the signal mechanism behind them was not evaluated.

The authors achieved their aims, and the results partially support their conclusions.

We agree that we must conduct future studies to evaluate our hypothesis.

The mouse ligatured periodontitis models differ from clinical periodontitis in human, this study supplies the basis for future research in human.

This is an important subject. We have previously expressed a concern on the mouse ligature model that the microbial composition of the mouse ligature did not mirror the human oral microbial composition. Therefore, we developed the maxillary topical application (MTA) model, in which human oral biofilm was directly applied to the maxillary gingiva. In this study, the newly developed MTA model was further dissected by single cell RNA seq, which revealed that the extracellular substances of human oral biofilm might be an important trigger of gingival inflammation. RESULT has been revised.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I appreciate the authors' efforts. I think it would be much better to simplify INTRODUCTION.

INTRODUCTION has been simplified as suggested.

Reviewer #2 (Recommendations For The Authors):

1. Many host cells participate in immune responses, such as gingival epithelial cells. AG fibroblast is not the only cell involved in the immune response, and the weight of its role needs to be clarified. So the expression in the conclusion should be appropriate.

RESPONSE: We agree with this comment. Our study identified the AG fibroblast–neutrophil–ILC3 axis as a previously unrecognized mechanism which could play an additional role in the complex interplay between oral barrier immune cells.

1. The main results should be included in the Abstract.

Abstract has been revised.

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

We thank all reviewers for constructive critiques. We plan to perform new experiments and revise our manuscript accordingly. The text and Figures are currently undergoing the revision process. Below highlights our revision plan.

eLife assessment

The findings of this article provide valuable information on the changes of cell clusters induced by chronic periodontitis. The observation of a new fibroblast subpopulation, which was named as AG fibroblasts, was quite interesting, but needs further evidence. The strength of evidence presented is incomplete.

We discovered a new subpopulation of gingival fibroblasts, named AG fibroblasts, using non-biased single cell RNA sequencing (scRNA-seq) of mouse gingival samples undergoing the development of ligature-induced periodontitis. AG fibroblasts exhibited a unique gene expression profile: [1] constitutive expression of type XIV collagen; and [2] ligatureinduced upregulation of Toll-Like Receptors and their downstream signals as well as chemokines such as CXCL12. Thus, we have hypothesized that AG fibroblasts initially sense the pathological stress including oral microbial stimuli and secrete inflammatory signals through chemokine expression.

The current manuscript examined the relationship between AG fibroblasts and oral barrier immune cells focusing on the chemokines and other ligands derived from AG fibroblasts and their putative receptors in those immune cells. Using scRNA-seq data mining programs, our data demonstrated the compelling evidence that AG fibroblasts should play a critical role in orchestrating the oral barrier immunity, at least at the early stages of periodontal inflammation.

We agree that it is important to explore the functional/pathological role of AG fibroblasts. In this revision, we further investigated the role of TLRs in the pathogen sensing mechanism of AG fibroblasts. To accomplish this goal, we applied a newly developed mouse model in which mice were exposed to the maxillary topical application (MTA) of oral microbial pathogens without the ligature placement. With 1 hr exposure with human oral biofilm, not with planktonic microbiota, the mice maxillary tissue exhibited measurable degradation as evidenced by the activation of cathepsin K. To dissect the role of TLRs, we applied the putative stimulants of TLR9 and TLR2/4 using the discrete MTA model. The scRNA-seq from the MTA model revealed that the application of unmethylated CpG oligonucleotide and P. gingivalis lipopolysaccharide (LPS), respectively, induced the activation of chemokines by AG fibroblast.

The revised manuscript reported this critical data with the detailed information. As such the additional figures and corresponding results, discussion and materials & methods were included.

Public Reviews:

Reviewer #1 (Public Review):

In this article, the authors found a distinct fibroblast subpopulation named AG fibroblasts, which are capable of regulating myeloid cells, T cells and ILCs, and proposed that AG fibroblasts function as a previously unrecognized surveillant to orchestrate chronic gingival inflammation in periodontitis. Generally speaking, this article is innovative and interesting, however, there are some problems that need to be addressed to improve the quality of the manuscript.

We appreciate this comment. As suggested, we further investigated the surveillant function of AG fibroblasts by reanalyzing the scRNA-seq data for stress sensing receptors such as Toll-Like Receptors (TLR). In the revision, we addressed the role of TLR in the activation of AG fibroblasts using a newly developed mouse model employing the maxillary topical application (MTA) of putative TLR stimulants. The new information clearly demonstrated that AG fibroblasts play a pivotal role as the surveillant and translating the pathogenic stimulants to oral barrier inflammation through chemokine expression.

Reviewer #2 (Public Review):

This study proposed the AG fibroblast-neutrophil-ILC3 axis as a mechanism contributing to pathological inflammation in periodontitis. However, the immune response in the vivo is very complex. It is difficult to determine which is the cause and which is the result. This study explores the relevant issue from one dimension, which is of great significance for a deeper understanding of the pathogenesis of periodontitis. It should be fully discussed.

We appreciate this comment. We expanded the current understanding of oral immune signal communication in Discussion and highlight how AG fibroblast may fit to it. To address this question, we expanded our investigation in the pathological signal detection by AG fibroblasts by employing the newly developed maxillary topical application (MTA) model. The revised manuscript contains the new information and expanded the discussion in the context of complex immune response.

Reviewer #1 (Recommendations For The Authors):

Detailed comments are listed below:

Abstract：<br /> I am confused about the expression of "human periodontitis-like phenotype". How does the authors define this concept? Periodontitis is a complex disease, despite that alveolar bone resorption is a typical manifestation of periodontitis, its characteristics remain to be further studied. I hope the authors can provide some detailed information about this concept or describe it in another way.

This is an important comment. Radiographically, human periodontitis is diagnosed by alveolar bone resorption from the cervical region, not from root apex. To highlight this, we present dental radiographs of human periodontitis as supplementary information. However, we agree with this comment, our statement should be limited to alveolar bone resorption pattern in Rag2KO and Rag2gcKO mice. Abstract be revised accordingly.

Introduction:<br /> It is recommended to simplify the first to third paragraphs, and briefly explain the functions of various types of cells in different stages of periodontitis, as well as the role of different cluster markers play across the time course of periodontal inflammation development.

Following this recommendation, INTRODUCTION has been simplified.

Results:<br /> 1. It is recommended to add HE staining and immunohistochemistry staining to observe the inflammation, tissue damage, and repair status from 0 to 7 days, so that readers can understand cell phenotype changes corresponding to the periodontitis stage. The observation index can include inflammation and vascular related indicators.

As recommended, representative histological figures were included. We further performed new immunohistochemistry experiment of mouse gingival tissue (D0, D1, D3, D7) highlighting the infiltration of CD45+ immune cells. We found that inflammatory vascular formation in the H&E histology, which was highlighted. To characterize the tissue damage, the histological sections were stained by picrosirius red to highlight the change in collagen connective tissue of PDL and gingiva.

1. Figure 1A-1D can be placed in the supplementary figure.

Combining the new data above, Figure 1 was revised as suggested.

1. I suggest the authors to put the detection of the existence of AG fibroblasts before exploring its relationship with other types of cells.

2. The layout of the picture should be closely related to the topic of the article. It is recommended to readjust the layout of the picture. Figure 1 should be the detection of AG cells and their proportion changes from 0 to 7 days. In other figures, the authors can separately describe the proportion changes of myeloid cells, T cells and ILCs, and explored the association between AG fibroblasts and these cell types.

As suggested, the presentation order of Figures and text was revised to bring the information about AG fibroblasts first. The chemokine-receptor analysis was moved below.

1. Please provide the complete form of "KT" in Line 162.

KT fibroblasts (fibroblasts keeping typical phenotype) was described in the text.

Methods:<br /> It is recommended to separately list the statistical methods section. The statistical method used in the article should be one-way ANOVA.

A separate statistical method section is created. As pointed out, we used one-way ANOVA with post-hoc Tukey test (when multiple groups were compared).

Discussion:<br /> I suggest the authors remove Figures 3-6 from the discussion section. For example, in Line 283, "(Figure 3 and 4)" should be removed.

Revised as suggested.

Reference:<br /> Some information for the references is missing. For example, "Lin P, et al. Application of Ligature-Induced Periodontitis in Mice to Explore the Molecular Mechanism of Periodontal Disease. Int J Mol Sci 22, (2021)" should be "Lin P, et al. Application of Ligature-Induced Periodontitis in Mice to Explore the Molecular Mechanism of Periodontal Disease. Int J Mol Sci 22, 8900 (2021)". It is necessary to recheck all references.

The reference has been checked for the accuracy and the omission pointed out was corrected. Although we used EndNote program, we found some more inaccuracy in the references that were manually corrected. We appreciate your suggestion.

Reviewer #2 (Recommendations For The Authors):

1. Many host cells participate in immune responses, such as gingival epithelial cells. AG fibroblast is not the only cell involved in the immune response, and the weight of its role needs to be clarified. So the expression in the conclusion should be appropriate.

Following this critique, we revised INTRODUCTION, DISCUSSION and CONCLUSION, to highlight how AG fibroblasts function within a comprehensive immune response network.

1. This study cannot directly answer the issue of the relationship between periodontitis and systemic diseases.

We agree with this critique. We either deleted or de-emphasized the relationship between periodontitis and systemic diseases throughout the text.

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Reply to the reviewers

_We have underlined the important points in the reviewer's comments. All responses have been read and authorized by all authors of this manuscript. Authors would like to thank the reviewers and the editor for their valuable time. We believe that the comments and suggestions from both reviewers will significantly improve SMorph and the manuscript. _

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

First of all, I want to apologize the authors and editor for my delay. Secondly, for clarity, I want to disclose that I am the author of the Fiji's 'Sholl Analysis' plugin, that the authors cite extensively (Ferreira et al, Nat Methods, 2014).

In this study, Sethi et al introduce a software tool - SMorph - for bulk morphometric analysis of neurons and glia (astrocytes and microglia), based on the Sholl technique. The authors compare it to the state-of-the-art in a series of validation experiments (stab wound injury), to conclude that it is 1000 times faster that existing tools. Empowered by the tool, the authors show that chronic administration of a tricyclic antidepressant (DMI) leads to structural changes of astrocytes in the mouse hippocampus. The paper is well written, the description of the tool is clear, and the authors make all of the source code available, as well as most of the imagery analyzed in the manuscript. The latter on its own, makes me really appreciative of the authors work.

We thank reviewer #1 for their careful reading of the manuscript and their comments.

**Major comments:**

A major strength of SMorph is that it leverages the Python ecosystem, which allow the authors take advantage of powerful python packages such as sklearn, without the need for external packages or tools. However, I have strong criticisms for the claims that are made in terms of speed and broad-applicability of the software, including PCA.

Speed:

The 1000x speed gains, assumes - for the most part -- that the processing in Fiji cannot be automated. This is false. I read the source code of SMorph, and with exception of the PCA analysis, all aspects of SMorph can be automated in Fiji, using any of Fiji's scripting languages to make direct calls to the Fiji and Sholl Analysis plugin APIs (See https://javadoc.scijava.org/) . Now, perhaps the authors do not have experience with ImageJ scripting, or perhaps we Fiji developers failed to provide clear tutorials and examples on how to do so. Or perhaps, there is something inherently cumbersome with Fiji scripting that makes this hard (e.g., there is a current limitation with the ImageJ2 version of 'Sholl Analysis' that does not make it macro recordable). It such limitations do exist, it is perfectly fine to mention them, but do contact us at https://forum.image.sc, if something is unclear. We do strive to make our work as re-usable as possible. Unfortunately our own research does not always allow us the time required to do so. Case in point, our scripting examples (e.g., https://github.com/tferr/ASA/blob/master/scripting-examples/3D_Analysis_ImageStack.py; https://github.com/tferr/ASA/blob/master/scripting-examples/3D_Analysis_ImageStack.py) are not well advertised. That being said, I am still surprised that in their side-by-side comparisons the authors were not able to automate more the processing steps (e.g., the ImageJ1 version of 'Sholl Analysis' remains fully functional and is macro recordable). If I misunderstood what was done, please provide the ImageJ macros you used. Also, I wanted to mention that i) semi-manual tracing with Simple Neurite Tracer (now "SNT"), can also be scripted (see https://doi.org/10.1101/2020.07.13.179325); and that ii) Fiji commands and plugins can also be called in native python using pyimagej (https://pypi.org/project/pyimagej/), see e.g., https://github.com/morphonets/SNT/tree/master/notebooks#snt-notebooks). Arguably, the fact that SMorph handles blob detection and skeletonization-based metrics directly is more advantageous from a user point of view. In Fiji, blob detection, skeletonization and Strahler analysis (https://imagej.net/Strahler_Analysis) of the skeleton are handled by different plugins. However, those are also fully scriptable, and interoperate well. The point that topographic skeletonization in Fiji can originate loops is valid, however the authors should know that such cycles can be detected and pruned programmatically using e.g., pixel intensities (see https://imagej.net/AnalyzeSkeleton.html#Loop_detection_and_pruning and the original publication (https://pubmed.ncbi.nlm.nih.gov/20232465/)

We completely agree with the reviewer’s assertion that most parts of the functionality of SMorph can be automated within imageJ as well, and in such comparison, the speed gains with SMorph will not be >1000X.

However, automating the analysis in imageJ is beyond the scope of the present manuscript. In fact, imageJ analysis comparison was not a part of our original manuscript at all. Upon presubmission inquiry to one of the affiliate journals of Review Commons, we were specifically asked to include a side-by-side comparison with “already available” methods. So, we decided to use ImageJ as it is, and automation, if any, was limited to simple macros to run a series of commands sequentially on batches of images. Although it is true that this analysis could be done much more efficiently with additional scripting, it would not have met the definition of “already available” tools. The imageJ analysis was performed in a way an average biologist with no programming experience would perform it, since that group will find SMorph most useful. In no way do we intend to imply that imageJ analysis can’t be made more efficient and automated. Perhaps it was not clear from the way the text was framed in the initial version of the manuscript. We will add additional text to make this point clearer.

On a side-note, in response to reviewer #2’s comments, we will perform the speed comparison on a per-image basis, so the speed gain (1080X) may change a little in the new comparison.

Broad applicability:

In our work, we made a significant effort to ensure that automated Sholl could be performed on any cell type: e.g., By supporting 2D and 3D images, by allowing repeated measures at each sampled distance, and by improving curve fitting. For linear profiles, we implemented the ability to perform polynomial fits of arbitrary degree, and implemented heuristics for 'best degree' determination. For normalized profiles, we implemented several normalizers, and alternatives for determining regression coefficients. We did not tackle segmentation of images directly (we did provide some accompanying scripts to aid users, see e.g. https://imagej.net/BAR) because in our case that is handled directly by ImageJ and Fiji's large collection of plugins. However, in SMorph, several of these parameters are hard-wired in the code. They may be suitable to the analyzed images, but they can be hardly generalized to other datasets. In detail: In terms of segmentation, SMorph is restricted to 2D images, scales data to a fixed 98 percentile, and uses a fixed auto-threshold method (Otsu). These settings are tethered to the authors imagery. They will give ill results for someone else using a different imaging setup, or staining method. In terms of curve fitting, the polynomial regression seems to be fixed at a 3rd order polynomial, which will not be suitable to different cell types (not even to all cells of 'radial morphology').

We have indeed hard-coded the parameters that the reviewer mentions, and we agree that we can perhaps give all options to the end-users to choose from. The decision was made to hard-code the parameters so that SMorph becomes very easy and minimalistic to use for the end-users. But the reviewer is right to point out that this may compromise the broad applicability and accuracy. We will update the code in the revised version of the manuscript to give the users control over choosing these parameters.

PCA:

The idea of making PCA analysis of Sholl-based morphometry accessible to a broader user base has merit and is welcomed. However, it has to be done carefully in a self-critic manner as opposed to a black-box solution. E.g., in the text it is mentioned that 2 principal components are used, in the tutorial notebook, 3. Why not provide intuitive scree plots that empower users with the ability to criticize choice? Also, it would be useful for users to understand which metrics correlate with each other, and their variable weights.

Reviewer #1’s suggestions would indeed make the PCA analysis more useful to the users. In the revised version of the code, we will provide additional data/plots to the user for making an informed choice of the significant principal components e.g. the elbow method, Ogive or Pareto plots, variable weights of different features in the principal components and correlation/covariance matrices.

When we showcased the utility of PCA to distinguish closely related morphology groups (as in Type-1 and Type-2 PV neurons), we had been unable to base the distinction on individual metrics, at least not in a robust manner (see Fig. S4 in Ferreira et al, 2014). A minor conundrum of the paper, is that it does not directly highlight the advantages of "analyzes in a multidimensional space". The differences between groups in the stab wound and DMI assays are such, that PCA is hardly needed: I.e., the differences depicted Fig2F,G are already significant, and already convey changes in "size and branch complexity" (as per PC1). The same argument applies to Fig. 5. The paper would profit from having this discussed.

PCA data indeed is not required to make any of the inferences we make in the paper and is superfluous. However, as mentioned in the discussion section of this manuscript, the low-dimensional PCA data can be used in future for other applications, e.g to cluster the astrocytes into morphometrically-defined subpopulations. SMorph can be further developed to perform real-time classification of these cells into morphometric clusters, which will allow the researchers to investigate clusters-specific gene expression, electrophysiology etc. Preliminary results from our lab do suggest that such clusters are differentially altered by stress and antidepressant treatments. However, these results are preliminary and are a part of a long-term future study. The data is really premature to publish at this stage, since it will require a lot of experimentation to show that these astrocyte subpopulations are indeed physiologically and functionally different. Nevertheless, we think that the utility of SMorph for such analyses may help others to come up with additional innovative ways to use the PCA data. Hence, we do believe that the community will benefit from the current release of SMorph having PCA. PCA data was shown in the figures just to demonstrate the functionality of SMorph. We will add additional text to make these points clearer.

Other:

- All metrics and parameters should be expressed in physical units (e.g.," radii increasing by 3 pixels", axes in Figure 2, 3, 5, S2) so that readers can directly interpret them.

In the revised manuscript, we will convert all units into actual physical distances.

- The paper would profit from the insights provided by Bird & Cuntz (https://pubmed.ncbi.nlm.nih.gov/31167149/)

We thank the reviewer for suggesting this paper. We will include this in the discussion of the manuscript.

**Minor comments:**

- Usage of RGB images (8-bit per channel) seems hardly justifiable. Aren't you loosing dynamic range of GFAP signal?

We agree that we could have captured the images at a higher dynamic range. However, for the changes we observe between treatment groups using GFAP immunoreactivity signal as presented in the manuscript, we do not see an advantage of using higher dynamic range. However, as the reviewer rightly pointed out, under certain conditions, imaging using a higher dynamic range may help and hence, we will include this recommendation in the materials and methods section.

- Please explain how MaxAbsScaler "prevents sub-optimal results"

Since morphometric features extracted from cell images either have different units or are scalar, we had to perform normalization before PCA. We will add further explanation in the methods section of the manuscript.

- The fact that automated batch processing can stall on a single bad 'contrast ratio' image seems rather cumbersome to deal with

This problem has been resolved in the current version of SMorph, which will be uploaded with the revised version of the manuscript.

- Please add a license to https://github.com/parulsethi/SMorph/. Without it, other projects may shy away from using SMorph

We will add a ____GPLv3 license

- "mounted on stereotax" should be "mounted on a stereotaxis device"?

We will make this change

- Ensure Schoenen is capitalized

We will make this change

Reviewer #1 (Significance (Required)):

I find the Desipramine results interesting. However, given the existing claims that DMI can modulate LTP, I regret that the authors did not look at structural modifications in hippocampal neurons (e.g., by performing the experiments in Thy1-M-eGFP animals). I understand, that doing so at this point would be a large undertaking.

Another manuscript from our lab__1, as well as work from other labs have shown that stress causes significant degenerative changes in hippocampal astrocytes__2,3__. In the light of these observations, we do believe that our observation of chronic antidepressant treatment inducing structural plasticity in astrocytes is significant. Structural alterations in neurons after DMI treatment are of interest. But in our experience, we have not seen gross morphological (dendritic arborization) changes in hippocampal neurons as a result of antidepressant drug treatments. Such changes are restricted to spine morphology and axonal varicosities, which is beyond the capabilities of SMorph. __

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

This paper addresses the challenge of automatic Sholl analysis of large dataset of multiple cell types such as neurons, astrocytes and microglia. The developed approach should improve the speed of morphology analysis compared to the state of the art without compromising on the accuracy. The authors present an interesting application of their tool to the morphological analysis of astrocytes following chronic antidepressant treatment. The paper is well written, and the tool presented could be beneficial for different applications and context. However, some major aspects should be addressed by the author concerning the description of the algorithms used and the quantification of the results.

We thank reviewer #2 for their careful reading of the paper and their comments.

**Major comments/Questions:**

1. In the Results and/or Methods sections, the author should better describe how their approach is different from state-of-the-art approaches in terms of algorithms used and how these difference impacts on the speed and accuracy of the analysis.

We will add these descriptions in the methods section in response to this comment as well as some comments from reviewer #1.

Imaging was performed on a Zeiss LSM 880 airyscan confocal microscope. Is this method robust to other types of imaging techniques, other microscopes, variable levels of signal-to-noise? This should be tested and quantified.

We will demonstrate the results obtained from images taken using different microscopes and imaging techniques, and quantify the outcome.

Manual cropping of the cells with ImageJ was used. However, in the methods section, the authors mention that other machine learning tools could be used for this task. Why were these tools not implemented in this paper in order to propose a fully automated analysis approach in combination with SMorph?

We have tried both the machine learning tools cited in this paper (one for DAB images and other for confocal images). However, in our experience, we do not get robust performance from these tools with our datasets, and these tools will perhaps need more optimization for broad applicability. We are developing an auto-cropping tool in-house, but that is beyond the scope of the current study. Another point is that these tools are tailor-made for astrocytes, and their integration into SMorph will restrict its applicability to just one cell type.

In the methods section you state that cropped cells need to have a good contrast ratio for automated batch processing. Could you define what a good contrast ratio is and characterize the performance of your approach for different contrast ratio?

In the revised manuscript, we will compare the images taken from multiple microscopes and quantify the outcome. We will change the text accordingly. As such, the comment on rejected cells referred to really poor quality images. In the revised manuscript, we will make specific recommendations on imaging parameters so that this should not be an issue at all.

It is mentioned that the analysis routine can be interupted by a cell with lower contrast ratio. This is a major drawback of the approach (but I think that it could be easily improved), as such interruptions may not be= practicable for many applications that need to rely on automated processing.

We have already rectified this problem and the updated version of SMorph will be uploaded with the revised manuscript.

Also, you should precise how the contrast ratio should be enhanced without modifying raw data in order to be processed with your approach. You suggest removing cells with lower contrast ratio from the analysis, but can this impact on the findings especially if some treatments impact on the detected fluorescence signal? Can you propose ways to improve the robustness of your approach to variable signal ratios?

It is indeed possible that removing cells from analysis, may in certain cases, affect the results. To rectify this, we are testing the method on images obtained from different microscopes and under different imaging conditions. From these analyses, we will deduce minimum recommendations for imaging conditions so that images don’t have to be edited/altogether removed from analysis for the software to work. In the materials and methods section, we will add these recommendations to the users on the optimal range of imaging parameters. This way, rejection/modification of images should not be an issue.

In the Results section, you describe the time necessary to perform different analysis. However, giving a total time in hours is not very informative as this will likely vary a lot depending on the size of the dataset, complexity of the images, etc. You should compare the average time per image for both methods and types of analysis.

We compared the total time required for the entire dataset, since SMorph is meant for batch-processing all the images at once. However, we can change the comparisons to time taken per image. We can divide the total time taken by SMorph by the number of images analysed. However, in our opinion, the time taken to initiate SMorph will make these comparisons inaccurate.

You state that for the number of branch point, the lower value of the measured slope when comparing SMorph and ImageJ was related to a constant overestimation of this parameter with ImageJ. How was this quantified? I think you should stress out more the comparison of both approaches with the manually annotated dataset.

In the revised version of this manuscript, we will include some examples of skeletonized images that overestimate the number of forks. We have observed this to be a recurring problem with the skeletonization tools we have tried in imageJ. This can be rectified in imageJ itself as pointed out by reviewer #1. However, that’s beyond the scope of the present study and will not fit the definition of comparison with “already available” methods.

How can you explain the differences in the 2D-projected Area, total skeleton length and convex hull between SMorph and ImageJ, which all show a slope around 0.83? Can you quantify the performance of both methods by comparing them with your manually annotated dataset?

In the revised version, we will include the correlation data between completely manual and SMorph comparisons. We will discuss these comparisons further in the manuscript and make specific conclusions about the accuracy.

In the introduction and discussion, you mention that you present a method that works on neurons, astrocytes and microglia. However, I don't see in the paper the comparison between the accuracy for all these cell types as you seem to have analyzed only the morphology of astrocytes.

In the revised manuscript, we will include the Sholl analysis comparison (imageJ vs SMorph) from images of neurons and microglia.

You mention that your method is quite sensitive to variation in contrast ratio. You should quantify the contrast ratio throughout the experiments and ensure that this is not biasing the SMorph analysis for some of the treatments.

We thank both reviewers for highlighting this issue in the initial version of SMorph. As mentioned in our response to point #6, we will perform additional analyses to make specific recommendations to the end users regarding imaging parameters so that SMorph can work on images as they are. As such, our comments on contrast ratio applied only to very poor quality images. If images are acquired conforming to the imaging parameters we will recommend in the revised manuscript, images can be analysed without any issues.

**Minor Points :**

1. Precise the exact inclusion and exclusion criteria for Soma detection and rephrase: "The high-intensity blobs were detected as a position of soma..." & "Boundary blobs coming from adjacent cells...".

We will add a complete explanation of blob detection and the exclusion criterion in the methods section.

Throughout the text, make sure to always refer to an analysis time per image or per cell and not only include absolute duration values without reference to the task at hand (e.g. in the discussion : SMorph took 40 second to complete the analysis... please state to which analysis you are exactly referring to and if applicable if it varies from cell to cell).

We will change all comparisons to time taken per cell. Text will be added to mention which datasets were used when any claims of speed are made.

When you state in the discussion that "Although some methods do allow Sholl analysis without manual neurite tracing, they still work on one cell at a time", please precise if the only aspect that is missing from this type of analysis is batch processing (looping through the data) or if there is a major obstacle to automate this technique. This is important a SMorph does proceed with the analysis one cell at a time but can work in a loop/batch.

We will elaborate further on our assertion regarding the challenges of using imageJ plugins for sholl analysis in large batches of cells.

Reviewer #2 (Significance (Required)):

This tool could very useful to researchers in the field of cellular neuroscience working with high-throughput analysis of microscopy data. The authors show some interesting improvements over existing methods. An improved quantitative characterization of the robustness of their approach would be of great importance to ensure the significance of this tool to a large community of researchers using different types of microscopes or studying different cell types.

My expertise is in the field of optical microscopy and high-throughput (automated) image analysis for neuroscience. My expertise to evaluate the biological findings in this study is very limited.

We thank reviewer #2 for their careful reading of the manuscript and their insightful comments. Growing evidence (clinical and preclinical) shows a significant reduction in astrocyte density in key limbic brain regions as a result of depression. We believe that the structural plasticity induced by chronic antidepressant treatment, as demonstrated in this manuscript, is an interesting novel plasticity mechanism that can negate deleterious effects of stress on astrocytes.

The improvements suggested by both reviewers will help us to greatly improve SMorph in the revised version of this manuscript.

References:

1. Virmani, G., D’almeida, P., Nandi, A. & Marathe, S. Subfield-specific Effects of Chronic Mild Unpredictable Stress on Hippocampal Astrocytes. doi:10.1101/2020.02.07.938472.
2. Czéh, B., Simon, M., Schmelting, B., Hiemke, C. & Fuchs, E. Astroglial plasticity in the hippocampus is affected by chronic psychosocial stress and concomitant fluoxetine treatment. Neuropsychopharmacology 31, 1616–1626 (2006).
3. Musholt, K. et al. Neonatal separation stress reduces glial fibrillary acidic protein- and S100beta-immunoreactive astrocytes in the rat medial precentral cortex. Dev. Neurobiol. 69, 203–211 (2009).

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Reply to the reviewers

Overall, we were pleased that the reviewers found our study carefully designed and interesting. We have addressed their comments below.

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

The manuscript by Kern, et al., demonstrates that phagocytosis in macrophages is regulated in part by the intermolecular distance of phagocytosis-promoting receptors engaging phagocytic targets. Cells expressing chimeric receptors containing cytosolic domains of Fc receptors (FcR) and defined ligand-binding DNA domains were used to drive phagocytosis of opsonized glass beads coated with complementary DNA ligands of defined spacing and number. These so-called origami ligands allowed manipulation of receptor spacing following engagement, which allowed the demonstration that tight spacing of ligands (7 nm or 3.5 nm) optimized signaling for phagocytosis. The study is carefully performed and convincing. I have a few technical concerns and minor suggestions.

1. __ It is assumed that the origami preparations were entirely uniform. How much variation was there? Is that supported by TIRF microscopy of origami preparations? Was the TIRF microscopy calibrated for uniformity of fluorescence (ie., shade correction)?__ Our laboratory, Dong et al., has extensively characterized the origami uniformity and robustness of these exact pegboards. This paper was just posted on bioRxiv (Dong et. al, 2021). We have also cited this paper in our revised manuscript in reference to the characterization of the DNA origami (Line 117).

We did not use any shade correction. Instead we only collected data from a central ROI in our TIRF field. To check for uniformity of illumination, we plotted the origami pegboard fluorescent intensity along the x and y axis. We observed very modest drop off in signal - the average signal intensity of origamis within 100 pixels of the edge is 76 ± 6% the intensity of origamis in a 100 pixel square in the center of the ROI. Fitting this data with a Gaussian model resulted in very poor R values. While this may account for some of the variation in signal intensity at individual points, we expect the normalized averages of each condition to be unaffected. We have amended the methods to describe this strategy (Lines 851-854).

(Image could not be uploaded)

__ Likewise, how much variation was there in the expression of the chimeric receptors? Large variation in receptor numbers per cell could significantly alter the quantitative studies. Aside from the flow sorting for cells expressing two different molecules, how were cells selected for analysis?__

We thank the reviewer for bringing up this point. We confirmed comparable receptor expression levels at the cell cortex of the DNA CAR-𝛾 and the DNA CAR-adhesion used throughout the paper. We also have confirmed that receptor levels at the cell cortex were similar for the large DNA CAR constructs used in Figure 6C-D. This data is now included in Figures S5 and S7. We have also altered the text to include this (lines 169-172):

Expression of the various DNA CARs at the cell cortex was comparable, and engulfment of beads functionalized with both the 4T and the 4S origami platforms was dependent on the Fc𝛾R signaling domain (Figure S5).

When quantifying bead engulfment, cells were selected for analysis based on a threshold of GFP fluorescence, which was held constant throughout analysis for each individual experiment. We have amended the “Quantification of engulfment” methods section to convey this (lines 921-923).

__ The scale of the origami relative to the cells is difficult to discern in Figures 2C and D. Additional text would be helpful to indicate, for example, that the spots on the Fig. 2D inset indicate entire origami rather than ligand spots on individual origami particles.__

Thank you for pointing this out, we see how the legend was unclear and have corrected it (lines 453-454), including specifically noting “Each diffraction limited magenta spot represents an origami pegboard.” We have also outlined the cell boundary in yellow to make the cell size more clear.

__ Figure 5 legend, line 482: How was macrophage membrane visualized for these measurements?__

We have added the following clarification (line 535-536): “The macrophage membrane was visualized using the DNA CAR𝛾, which was present throughout the cell cortex.”

__ line 265: "our data suggest that there may be a local density-dependent trigger for receptor phosphorylation and downstream signaling". This threshold-dependent trigger response was also indicated in the study of Zhang, et al. 2010. PNAS.__

The Zhang et al. study was influential in our study design, and we wish to give the appropriate credit. Zhang et al. found that a sufficient amount of IgG is necessary to activate late (but not early) steps in the phagocytic signaling pathway. In contrast, our study addresses IgG concentration in small nanoclusters. We find that this nanoscale density affects receptor phosphorylation. Thus, we think these two studies are distinct and complementary.

Lines 283-287 now read:

While this model has largely fallen out of favor, more recent studies have found that a critical IgG threshold is needed to activate the final stages of phagocytosis (Zhang et al., 2010). Our data suggest that there may also be a nanoscale density-dependent trigger for receptor phosphorylation and downstream signaling.

__ line 55: Rephrase, “we found that a minimum threshold of 8 ligands per cluster maximized FcgR-driven engulfment.” It is difficult to picture how a minimum threshold maximizes something.__

We now state “we found that 8 or more ligands per cluster maximized FcgR-driven engulfment.”

__ line 184: Rephrase, "we created... pegboards with very high-affinity DNA ligands that are predicted not to dissociate on a time scale of >7 hr". Remove "not".__

Thank you for pointing this out, it is now correct.

Reviewer #1 (Significance (Required)):

This study provides a significant advance in understanding about the molecular mechanisms of signaling for particle ingestion by phagocytosis.

--

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

The manuscript on “Tight nanoscale clustering of Fcg-receptors using DNA origami promotes phagocytosis" studies how clustering and nanoscale spacing of ligand molecules for a chimeric Fcg-receptors influence the phagocytosis of functionalized silicon beads by macrophage cell lines. The basis of this study is the design of a chimeric Fc-receptor (DNA-CARg) comprising an extracellular SNAP-tag domain that can be loaded with single-stranded (ss) DNA, the transmembrane part of CD86 and the cytosolic part of the Fc-receptor g-chain containing an immunoreceptor tyrosine-based activation motif (ITAM) as well as a C-terminal green fluorescent protein (GFP). As control the authors used a similar designed DNA-CAR that is lacking the intracellular ITAM-containing FCg tail. The chosen target for this chimeric DNA-CAR, are silicon beads covered by a lipid bilayer that contains biotin-labelled lipids that, via Neutravidin, can be loaded with a biotinylated DNA origami pegboard displaying complimentary ss-DNA as ligand for the DNA-CAR. The DNA origami pegboard contains four ATTO647N fluorescence for visualization and the ssDNA ligand in different quantities and spacing. Using these principles, the authors study how ligand affinity, concentration and spacing influence the activation of the DNA-CARg and the engulfment of the loaded beads.

The authors show that bead engulfment is increased between 2 till 8 ssDNA ligands on the pegboard. After this, ligand numbers do not play a role anymore in the engulfment. They then study the role of the ligand spacing using pegboards that either contain 4 single strand DNA ligands in close (7nm/3,5nm) proximity or a more spaced version using 21/17,5 nm or 35/38,5 nm. The authors find that the bead engulfment is maximally and positively affected by the close spacing of the ssDNA ligands. In their final experiments the authors vary the design of the DNA-CARs by tetramerization of the ITAM-containing Fcg-signaling subunit. In their discussion the authors mention different possibilities for the effect of spacing on the engulfment process.

I think that, in general, this is an interesting study. However, it has some caveats and open issues that should be clarified before its publication.

**Major comments**

1. __ As a general comment, it is somewhat a pity that the authors did not use the endogenous FcR as a control. It would have been quite easy for the authors to place the SNAP-tag domain on the Fcg extracellular domain which would allow to do all their experiments in parallel, not only with the DNA-CAR, but also with a DNA-containing wild type receptor. Such a control would be important because, by using a CD86 transmembrane domain, the authors do not know whether the nanoscale localization of their chimeric receptors is reflecting that of the endogenous Fcg receptor.__

We agree with the reviewer completely. We have repeated experiments shown in Figure 4A with a DNA-CAR containing the Fc𝛾 transmembrane domain instead of CD86 as the reviewer suggests. We also included a DNA-CAR version of the Fc𝛾R1 alpha chain, although this construct was not expressed as well as the others. These data are now included in Figure S5, and referenced in lines 167-168.

__ An important issue that is discussed by the authors but not addressed in this manuscript is whether the different amount and spacing of the ligand is only impacting on signaling or also on the mechanical stress of the cells. Indeed, mechanical stress on the cytoskeleton arrangement could influence the engulfment process. For this, it would be very important to test that the different bead engulfment, for example, those shown in Fig. 4, is strictly dependent on signaling kinases. The authors should repeat the experiment of Fig. 4 a and b in the presence or absence of kinase inhibitors such as the Syk inhibitor R406 or the Src inhibitor PP2 to show whether the different phase of engulfment is dependent on the signaling function of these kinases. This crucial experiment is clearly missing from their study.__

We agree this is an interesting point. We find that ligand spacing affects receptor phosphorylation; however this does not preclude effects on downstream aspects of the signaling pathway. We will clarify this by adding the following comment to the manuscript (line 299-301):

While our data pinpoints a role for ligand spacing in regulating receptor phosphorylation, it is possible that later steps in the phagocytic signaling pathway are also directly affected by ligand spacing.

The DNA-CAR-adhesion in Figure 1 strongly suggests that intracellular signaling is essential for phagocytosis. We have now included additional controls using this construct as detailed in our response to point 3 below. Unfortunately, Src and Syk inhibitors or knockout abrogate Fc𝛾R mediated phagocytosis (for example, PMIDs 11698501, 9632805, 12176909, 15136586) and thus would eliminate phagocytosis in both the 4T and 4S conditions. This precludes analysis of downstream steps in the phagocytic signaling pathway.

__ Another problem of this study is that the authors show in Fig. 1A the control DNA-CAR-adhesion but then hardly use it in their study. For example, the crucial experiments shown in Fig. 4 should be conducted in parallel with DNA-CAR-adhesion expressing macrophage cells. This study could provide another indication whether or not ITAM signaling is important for the engulfment process.__

We have added this control. It is now included in Figure S5 and S7. Figure 3D also shows that the DNA-CAR-adhesion combined with the 4T origami pegboards does not activate phagocytosis and we have amended the text to make this more clear (line 152).

__ Another important aspect is how the concentration of the loaded origami pegboard is influencing the engulfment process. In particular, it would be interesting to show the padlocks with different spacings such as the 4T closed spacing versus 4s large spacing show a different dependency on the concentration of this padlock loading on the beads. This would be another important experiment to add to their study.__

We agree that this is an interesting question. We suspect that at a very high origami density, 4S signaling would improve, and potentially approach the 4T. However, we are currently coating the beads in saturating levels of origami pegboards. Thus we cannot increase origami pegboard density and address this directly.

**Minor comments:**

1. __ The definition of the ITAM is Immunoreceptor Tyrosine-based Activation Motif and not "Immune Tyrosine Activation Motif" as stated by the authors.__ We have corrected this.

__ The authors discuss that it is the segregation of the inhibitory phosphatase CD45 from the clustered Fc receptors is the major mechanism explaining their finding that 4T closed spacing is more effective than 4s large spacing. With the event of the CRISPR/Cas9 technology it is trivial to delete the CD45 gene in the genome of the RAW264.7 macrophage cell line used in this study and I am puzzled why they author are not conducting such a simple but for their study very important experiment (it takes only 1-2 month to get the results).__

This experiment may be informative but we have two concerns about its feasibility. First, CD45 is a phosphatase with many different roles in macrophage biology, including activating Src family kinases by dephosphorylating inhibitory phosphorylation sites (PMID 8175795, 18249142, 12414720). Second, CD45 is not the only bulky phosphatase segregated from receptor nanoclusters. For example, CD148 is also excluded from the phagocytic synapse (PMID 21525931). CD45 and CD148 double knockout macrophages show hyperphosphorylation of the inhibitory tyrosine on Src family kinases, severe inhibition of phagocytosis, and an overall decrease in tyrosine phosphorylation (PMID 18249142). CD45 knockout alone showed mild phenotypes in macrophages. We anticipate that knocking out CD45 alone would have little effect, and knocking out both of these phosphatases would preclude analysis of phagocytosis. Because of our feasibility concerns and the lengthy timeline for this experiment, we believe this is outside of the scope of our study.

In our discussion, we simplistically described our possible models in terms of CD45 exclusion, as the mechanisms of CD45 exclusion have been well characterized. This was an error and we have amended our discussion to read (lines 335-343):

As an alternative model, a denser cluster of ligated receptors may enhance the steric exclusion of the bulky transmembrane proteins like the phosphatases CD45 and CD148 (Bakalar et al., 2018; Goodridge et al., 2012; Zhu, Brdicka, Katsumoto, Lin, & Weiss, 2008).

Reviewer #2 (Significance (Required)):

The innovative part of this study is the combination of SNAP-tag attached, chimeric Fc-receptor with the DNA origami pegboard technology to address important open question on receptor function.

**Referees cross-commenting**

I find most of my three reviewing colleagues reasonable

I also agrée to Reviewer #1 comments 2

Likewise, how much variation was there in the expression of the chimeric receptors? Large variation in receptor numbers per cell could significantly alter the quantitative studies. Aside from the flow sorting for cells expressing two different molecules, how were cells selected for analysis?

But I want to add it is not only the amount of receptors but ils the nanoscale location that is key to receptor function

We have ensured that all receptors are trafficked to the cell surface. We have also measured their intensity at the cell cortex as discussed in response to Reviewer 1.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

This is a very nicely done synthetic biology/biophysics study on the effect of ligands spacing on phagocytosis. They use a DNA based recognition system that the group has previously use to investigate T cell signaling, but express the SNAP tag linked transmembrane receptor in a macrophage cell line and present the ligands using DNA origami mats to control the number and spacing of complementary ligands that are designed to be in the typical range for low or high affinity FcR, a receptor that can trigger phagocytosis. The study offers some very nice quantitative data sets that will be of immediate interest to groups working in this area and, in the future, for design of synthetic receptors for immunotherapy applications. Other groups are working on similar platform for TCR. I don't feel there is any need for more experiments, but I have some questions and suggestions. Answering and considering these could clarify the new biological knowledge gained.

We thank the reviewer for their support of our manuscript. Given the reviewer’s statement that no new experiments are required, we have answered their questions to the best of our ability given the current data. Should the editor decide that any of these topics require experimental data to enhance the significance of the paper, we are happy to discuss new experiments.

Reviewer #3 (Significance (Required)):

I think the significance would be increased by addressing these questions, that would help understand how the synthesis system described related to other system directed as similar questions and more natural settings.

1. __ The densities of the freely mobile DNA ligands required to trigger phagocytosis is quite high. Was the length of the DNA duplexes optimized? The entire complex for both the intermediate and high affinity duplexes seems quite short, perhaps The extracellular domain of the DNA-CAR (SNAP tag and ssDNA strand) are approximately 10 nm (PMID 28340336). The biotinylated ligand ssDNA is attached to the bilayer via neutravidin, resulting in a predicted 14 nm intermembrane spacing. The endogenous IgG FcR complex is 11.5 nm. Bakalar et al (PMID 29958103) tested the effect of antigen height on phagocytosis and found that the shortest intermembrane distance tested (approximately 15 nm) was the most effective. As the reviewer notes, the optimal distance between macrophage and target may be larger than our DNA-CAR. However we think the intermembrane spacing in our system is within the biologically relevant range.

We saw robust phagocytosis at 300 molecules/micron of ssDNA, which is similar to the IgG density used on supported lipid bilayer-coated beads in other phagocytosis studies (PMID 29958103, 32768386). As the reviewer noticed, this is significantly higher than ligand density necessary to activate T cells (PMID 28340336). We have added a comment on ligand density to lines 96-97.

__ Are the origami mats generally laterally mobile on the bilayers. If so, what is the diffusion coefficient? Can one detect the mats accumulating in the initial interface between the bead and cell, particularly in cased where there is no phagocytosis? Would immobility of the mats make them more efficient at mediating phagocytosis compared to the monodispersed ligands, which I assume are highly mobile and might even be "slippery".__

We have confirmed that our bead protocol generally produces mobile bilayers, where his-tagged proteins can freely diffuse to the cell-bead interface (see accumulation of a his-tagged FRB binding to a transmembrane FKBP receptor at the cell-bead synapse below). We can qualitatively say that the origamis appear mobile on a planar lipid bilayer (see Dong et. al 2021 and images below). Directly measuring the diffusion coefficient on the beads is extremely difficult because the beads themselves are mobile (both diffusing and rotating), and cannot be imaged via TIRF. We do not see much accumulation of the origami at cell-bead synapses. This could reflect lower mobility of the origamis, or could be because the relative enrichment of origamis is difficult to detect over the signal from unligated origamis.

Overall, we expect the origami pegboards (tethered by 12 neutravidins) are less mobile than single strand DNA (tethered by a single neutravidin, supported by qualitative images below). We are uncertain whether this promotes phagocytosis. At least one study suggests that increased IgG mobility promotes phagocytosis (PMID 25771017). However, the zipper model would suggest that tethered ligands may provide a better foothold for the macrophage as it zippers the phagosome closed (PMID 14732161). Hypothetically, ligand mobility could affect signaling in two ways - first by promoting nanocluster formation, and second by serving as a stable platform for signaling as the phagosome closes. Since our system has pre-formed nanoclusters, the effect of ligand mobility may be quite different than in the endogenous setting.

(Image could not be uploaded)

In the above images, a 10xHis-FRB labeled with AlexaFluor647 was conjugated to Ni-chelating lipids in the bead supported lipid bilayer. The macrophages express a synthetic receptor containing an extracellular FKBP and an intracellular GFP. Upon addition of rapamycin, FRB and FKBP form a high affinity dimer, and FRB accumulates at the bead-macrophage contact sites.

(Image could not be uploaded)

In the above images, single molecules were imaged for 3 sec. The tracks of each molecule are depicted by lines, colored to distinguish between individual molecules. The scale bar represents 5 microns in both panels.

__ Breaking down the analysis into initiation and completion is interesting. When using the non-signalling adhesion constructs, would they get to the initiation stage or would that attachment be less extensive than the initiation phase.__

This is an interesting question. While we did not include the DNA-CAR-adhesion in our kinetic experiments, we have now quantified the frequency of cups that would match our ‘initiation’ criteria in 3 representative data sets where macrophages were fixed after 45 minutes of interaction with origami pegboard-coated beads. We found that an average of 16/125 of 4T beads touching DNA-CAR-adhesion macrophages met the ‘initiation’ criteria and an average of 2/125 were eaten (14% total). In comparison, we examined 4T beads touching DNA CAR𝛾 macrophages and found that on average 23/125 met the ‘initiation’ criteria, and 45/125 were already engulfed (54%). This suggests that the DNA-CAR-adhesion alone may induce enough interaction to meet our initiation criteria, but without active signaling from the FcR this extensive interaction is rare. We have added this data in a new Figure S6 and commented on this in lines 213-215.

__ It would be interesting to put these results in perspective of earier work on spacing with planar nanoarrays, although these can't be applied to beads. For integrin mediated adhesion there was a very distinct threshold for RGD ligand spacing that could be related to the size of some integrin-cytoskeletal linkers (PMID: 15067875). On the other hand, T cell activation seemed more continuous with changes in spacing over a wide range with no discrete threshold (PMID: 24117051, 24125583) unless the spacing was increased to allow access to CD45, in which case a more discrete threshold was generated (PMID: 29713075). The results here for phagocytosis with the very small ligands that would likely exclude CD45 seems to be more of a continuum without a discrete threshold, although high densities of ligand are needed. This issue of continuous sensing vs sharp threshold is biologically interesting so would be good assess this by as consistent standards are possible across systems.__

We agree that this is an interesting body of literature worth adding to our discussion. We have added a paragraph that puts our study in the context of prior work on related systems, including these nanolithography studies (Line 364-382):

How does the spacing requirements for Fc𝛾R nanoclusters compare to other signaling systems? Engineered multivalent Fc oligomers revealed that IgE ligand geometry alters Fcε receptor signaling in mast cells (Sil, Lee, Luo, Holowka, & Baird, 2007). DNA origami nanoparticles and planar nanolithography arrays have previously examined optimal inter-ligand distance for the T cell receptor, B cell receptor, NK cell receptor CD16, death receptor Fas, and integrins (Arnold et al., 2004; Berger et al., 2020; Cai et al., 2018; Deeg et al., 2013; Delcassian et al., 2013; Dong et al., 2021; Veneziano et al., 2020). Some systems, like integrin-mediated cell adhesion, appear to have very discrete threshold requirements for ligand spacing while others, like T cell activation, appear to continuously improve with reduced intermolecular spacing (Arnold et al., 2004; Cai et al., 2018). Our system may be more similar to the continuous improvement observed in T cell activation, as our most spaced ligands (36.5 nm) are capable of activating some phagocytosis, albeit not as potently as the 4T. Interestingly, as the intermembrane distance between T cell and target increases, the requirement for tight ligand spacing becomes more stringent (Cai et al., 2018). This suggests that IgG bound to tall antigens may be more dependent on tight nanocluster spacing than short antigens. Planar arrays have also been used to vary inter-cluster spacing, in addition to inter-ligand spacing (Cai et al., 2018; Freeman et al., 2016). Examining the optimal inter-cluster spacing during phagosome closure may be an interesting direction for future studies.

--

Additional experiments performed in revision

In addition to these reviewer comments, we have added additional controls validating the DNA-CAR-4x𝛾 used in Figure 6c,d. We compared the DNA-CAR-4x𝛾 to versions of the DNA-CAR-1x𝛾-3x𝛥ITAM construct with the functional ITAM in the second and fourth positions (see the schematics now included Figure S7). We found that four individual receptors with a single ITAM each were able to induce phagocytosis regardless of which position the ITAM was in. However the DNA-CAR-4x𝛾 construct, which also contains 4 ITAMs, was not. This further validates the experiment presented in 6c,d. We also fixed minor errors we discovered in the presentation of data for Figures 1C and S1A.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

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Reply to the reviewers

__Reviewer #1: __ __ **Major concerns:**

1) This manuscript has some overlap with another manuscript from the same group recently submitted to EMBO Reports. Although I believe both manuscripts have sufficient elements to justify publication of two papers, I strongly recommend that these publications are made back-to-back and they should be discussed in context with one-another.

__

We agree that this manuscript is distinct from but highly complementary to our manuscript on innate immunity in the long-lived mitochondrial mutants, which has been invited for revision at EMBO Reports. According to this suggestion, we have arranged for these papers to be considered for publication at the same time in EMBO Reports and Life Science Alliance. We have updated the discussions of both manuscripts to incorporate the findings of the other manuscript.

__ 2) How is ATFS-1 function regulated in long-lived worms or under multiple stress conditions? Is there a common regulator such as oxidative stress or mitochondrial dysfunction? Both manuscripts would benefit from a clear understanding on how ATFS-1 is controlled under conditions where mitochondrial function is altered. Is mitoUPR required for this activation? If so, is mitoUPR upregulated in all interventions where ATFS-1 has been shown to play a role in stress response. __

We have previously used a reporter strain to determine which external stressors activate ATFS-1. The reporter strain has a transgene that links the promoter of the ATFS-1 target gene hsp-6 to GFP (Phsp-6::GFP) such that these worms exhibit increased fluorescence whenever ATFS-1 is activated. After exposing these worms to heat, cold, osmotic stress, anoxia, oxidative stress, starvation, ER stress and bacterial pathogens, we only observed increased fluorescence after exposure to oxidative stress (Dues et al. 2016, Aging). Here, we show that constitutive activation of ATFS-1 results in increased resistance not only to oxidative stress but also ER stress, osmotic stress, anoxia and bacterial pathogens (fast kill assay). Thus, ATFS-1 activation does not just protect against stresses that lead to its activation. Notably, the constitutively active atfs-1 mutants (et15 and et17) exhibit activation of the mitoUPR under unstressed conditions (e.g. upregulation of hsp-6 in Fig. 1A; increased fluorescence of hsp-6 and hsp-60 reporter strains in Rauthan et al. 2013, PNAS; upregulation of many other stress pathway target genes Fig. 2). It is likely that the activation of the mitoUPR and downstream stress response pathways under unstressed conditions results in the increased resistance to stress that we observe. We have included these points in the revised manuscript.

__Is there any intervention that controls longevity and does not trigger ATFS-1 response?

__

When we compared RNA-seq data on a panel of long-lived mutants representing multiple pathways of lifespan extension to ATFS-1 target genes (defined as genes that are upregulated by spg-7 RNAi in an ATFS-1 dependent manner from Nargund et al. 2012, Science), we found that seven of the nine long-lived mutants that we examined showed enrichment of ATFS-1 target genes (clk-1, isp-1, nuo-6, daf-2, glp-1, ife-2) while two did not (eat-2, osm-5) (Fig. 5). Interestingly, in six of these seven strains (all except ife-2), there is an increase in reactive oxygen species (ROS) that contributes to their longevity (treatment with antioxidants decreases their lifespan; Yang and Hekimi 2010, PLoS Biology; Zarse et al. 2012, Cell Metabolism; Wei and Kenyon 2016, PNAS). This observation is consistent with the idea that ROS/oxidative stress is sufficient to activate ATFS-1/mitoUPR. We have previously shown that exposure to a mild heat stress (35°C, 2 hours) or osmotic stress (300 mM, 24 hours) can extend lifespan but does not increase expression of the ATFS-1 target gene hsp-6 (Dues et al. 2016, Aging). Thus, there are multiple examples in which a genetic mutation or intervention increases longevity but does not trigger upregulation of ATFS-1 target genes. We have updated the manuscript to include these points.

__3) In Fig. 3, some of these genes appear to be unspecifically associated with different stressors. Therefore, it is difficult to rule out the participation of ATFS-1 in specific stress responses without looking at specific stress-responsive genes or a wider range of genes. For example, the conclusion that ATFS-1 does not control osmotic stress gene expression response comes from looking at 3 genes: sod-3, gst-4 and Y9C9A.8. gst-4 does not appear to be directly controlled by ATFS-1 regardless of the stressor. sod-3 is also upregulated by oxidative stress and Y9C9A.8 by anoxia. On the other hand, somewhat contradicting the authors' conclusions that ATFS-1 does not participate in osmotic stress response based on these 3 genes, ATFS-1 appears to be required for osmotic stress resistance.

__

In this experiment, we treated wild-type and atfs-1 deletion mutants with six different stressors (oxidative stress, bacterial pathogens, heat stress, osmotic stress, anoxia, and ER stress), isolated mRNA and then examined the expression of 14 different stress response genes. To select these genes, we chose a combination of the most established target genes of the stress response pathways that we examined in Figures 1/2, and genes that we had previously shown to be upregulated by specific stresses using fluorescent reporter strains (Dues et al. 2016, Aging). These genes included hsp-6, hsp-4, hsp-16.2, sod-3, gst-4, nhr-57, Y9C9A.8, trx-2, ckb-2, gcs-1, sod-5, T24B8.5, clec-67 and dod-22. To determine if ATFS-1 is required for gene upregulation in response to any of the six different stressors, we first identified which of these stress genes is significantly upregulated in response to each stressor and then looked to see if this upregulation is reduced or prevented by atfs-1 mutation. We found that there were multiple examples of this for both oxidative stress and bacterial pathogen stress, but not for other stresses. We selected three representative genes to display in Figure 3. Nonetheless, it is possible that there are genes that we didn’t examine that are upregulated by the other four stressors in an ATFS-1-dependent manner. To definitively address this question, one would have to do RNA sequencing on wild-type and atfs-1(gk3094) worms comparing untreated and stressed, but this is beyond the scope of the current manuscript. We have updated the manuscript to include these points, and noted the possibility that there are genes, which we didn’t measure, that are upregulated by the other four stressors in an ATFS-1-dependent manner. We have also included the qPCR data for all 14 genes for each of the six external stressors in Supplemental Figures S3-S8.

__ **Minor concerns:**

1) The paragraph starting in line 107 is confusing. They write that "Constitutive activation of ATFS-1 in atfs-1(et 15) and atfs-1(et17) mutants resulted in upregulation of most of the same genes that are upregulated in nuo-6 mutants, except for gst-4" and later they state that "Activating the mitoUPR through the nuo-6 mutation, or through the constitutively-active ATFS-1 mutants did not significantly increase the expression of target genes from the ER-UPR (hsp-4; Fig. 1B) or the cyto-UPR (hsp-16.2; Fig. 1C)." I understand the upregulation of ER-UPR and cyto-UPR is not statistically significant (isn't it for hsp-16.2?), but the first sentence is not accurate if statistics is considered.

__

To clarify this, we have modified the first sentence to describe which genes are significantly upregulated in atfs-1(et15) mutants, and separately describe the findings for atfs-1(et17) mutants in the second sentence. The results for hsp-16.2 are not significant because this gene shows highly variable expression between replicates and can be induced 60-fold. We have noted this in the text as well.

__ 2) The authors should discuss why they think atfs-1(et15) gain-of-function mutant exhibited decreased resistance to chronic oxidative stress, while it is protected from acute oxidative stress. In fact, the et15 allele differs in many aspects in relation to the et17 and in some cases it behaves similarly to the gk3094 loss-of-function allele.

__

While atfs-1(et15) and atfs-1(et17) mutants generally show similar results, they also exhibit differences. We previously used RNA sequencing to examine gene expression in these two strains. We found that atfs-1(et15) mutants have far more extensive changes in gene expression than atfs-1(et17) mutants (6227 differentially expressed genes versus 958 differentially expressed genes). It is possible that the et15 mutation is more disruptive to the mitochondrial targeting sequence than et17, thereby resulting in increased nuclear localization and more gene expression changes. The additional gene expression changes in the atfs-1(et15) mutant may contribute to their decreased resistance to chronic oxidative stress. We have included these points in the revised manuscript.

__ 3) Fig 4I is very similar to Fig. 6A of the other manuscript which strengthen the notion that ATFS-1 is not required (it is rather detrimental) for bacterial pathogen response when no underlying stress (most likely oxidative) occurs.

__

Yes, our results indicate that ATFS-1 is not required for wild-type survival of bacterial pathogen exposure. This is consistent with our findings in the other manuscript that baseline expression of innate immunity genes does not depend on ATFS-1 (innate immunity gene expression is similar between wild-type and atfs-1(gk3094) mutants). We have updated the manuscript to emphasize these points.

__ 4) In the paragraph starting in line 213, the authors conclude that "ATFS-1 is sufficient to protect against oxidative stress, osmotic stress, anoxia, and bacterial pathogens but not heat stress". The results do not unequivocally support a participation of ATFS-1 in oxidative stress or bacterial pathogen response, given the responses vary depending on the allele or condition.

__

We have modified this sentence by replacing “activation of ATFS-1 is sufficient to protect” with “activation of ATFS-1 can protect” to indicate that we didn’t observe protection in all cases.

__ 5) "Combined, this indicates that ATFS-1 does not play a major role in lifespan determination in a wild-type background despite having an important role in stress resistance." It actually does, since ATFS-1 gain-of-function decreases lifespan.

__

We have rewritten this sentence to say that constitutive activation of ATFS-1 does not extend lifespan, despite increasing resistance to multiple stresses.

__

__

__ __

__6) Paragraph starting in line 359 needs to be discussed in light of the results of the other manuscript submitted by the authors to EMBO.

__

Combined these two manuscripts indicate that baseline levels of innate immunity are dependent on the p38-mediated innate immune signaling pathway, and not dependent on ATFS-1. This idea is supported by the fact that deletion of atfs-1 does not decrease resistance to bacterial pathogens and does not reduce the expression of innate immunity genes. In contrast, disrupting genes involved in the p38-mediated innate immune signaling pathway does decrease resistance to bacterial pathogens and does decrease the expression of innate immunity genes. We have updated this paragraph to include these points and reference the findings from our manuscript on innate immunity in the long-lived mitochondrial mutants.

__ 7) In Fig. 1C, it appears that atfs-1 loss of function increases hsp-16.2. Is that significant?

__

While there is a strong trend towards increased hsp-16.2 expression in atfs-1(gk3094) mutants, this difference did not reach significance because this gene shows highly variable expression and can be induced 60-fold.

__ 8) In Fig. 2, 5 and S1, it would be interesting to build one single Venn Diagram with all the lists of genes to see if there are common genes associated with multiple pathways and if there are many ATFS-1 target genes not associated with these classical stress or longevity pathways.

__

While we would be very interested in performing this type of visualization, weighted Venn diagrams with more than 3 or 4 groups are challenging to generate and more challenging to interpret. Instead, we have generated an UpSetR plot to demonstrate the number of overlapping genes between each of the stress response pathways, as well as how many ATFS-1 target genes are not involved in stress response. We have included this plot in Figure 2, Panel I. We have also generated simpler figure to show the overlap between pairs of stress response pathways (Figure S1). In addition, we have also added Table S4 with these gene lists.

__ 9) In Fig. 2, 5 and S1: What are the p values referred to?

__

The p-values indicate the significance of the difference between the observed number of overlapping genes between the two gene sets, and the expected number of overlapping genes if the genes were picked at random. We have clarified this in the manuscript.

__ 10) In paragraph starting in line 85, the authors should include references that evidence the genes are bona fide markers of the stress response pathways.

__

We have added references for each of the genes that we examined to link it to the associated stress response pathway.

__ 11) Tables S2 and S3 are missing. __

Tables S2 and S3 were uploaded as Excel spreadsheets, not included with the supplemental figures as the other supplementary Tables were. We apologize that these were difficult to locate. In the revision, Table S1 is in the manuscript file, while Table S2 to S6 will be uploaded as separate files.

__ __

__Reviewer #2:

**Major comments:**

The only major conclusion that I would qualify is "ATFS-1 serves a vital role in organismal survival of acute stresses through its ability to activate multiple stress response pathways"-the data, as presented, does not make clear whether ATFS-1 directly activates these pathways (ie, by binding response elements in genes in those pathways), or indirectly influences them by altering the physiology of the worm).

__

We agree that our data does not determine precisely how ATFS-1 acts to modulate the expression of the different stress response pathways. To determine the extent to which ATFS-1 might be able to bind directly to the target genes of other stress response pathways, we have compared the ChIP-seq results for ATFS-1 to ChIP-seq studies for other stress responsive transcription factors (DAF-16, SKN-1, HSF-1, HIF-1, ATF-7). We found that in each case there are sets of genes that can be bound by both transcription factors. This suggests that ATFS-1 may be direct regulating at least some of the target genes from other stress response pathways. We have updated our manuscript to include these points and included the ChIP-seq data comparisons in Figure S2.

__ **Minor comments:**

In abstract, consider broadening/re-wording "Gene expression changes resulting from the activation of the mitoUPR are mediated by the transcription factor ATFS-1/ATF-5." Because a naïve reader may understand this to suggest that ATFS-1 is activated only by mitochondrial protein misfolding.

__

In this sentence we are describing the role of ATFS-1 in mediating the gene expression changes resulting from the activation of the mitoUPR. We would be happy to modify the sentence if this is unclear.

__Please indicate whether strains were outcrossed, and how often.

__

We have added these details to our materials and methods.

__ How was "young adult" defined? Were worms synchronized, and if so, how?

__

Young adult worms are picked on day 1 of adulthood before egg laying begins. The worms were not synchronized, but picked visually as close to the L4-adult transition as possible. We have added these details to our method section.

__ For the gene expression experiments, do I understand correctly that FUDR was used only for oxidative stress and adult day 2 experiments? Please clarify.__

Yes, that is correct. FUdR was used for these samples because (1) with the 2-day duration of this stress, worms can produce progeny which would complicate the collection of the experimental worms; and (2) 4 mM paraquat often results in internal hatching of progeny when FUdR is absent, which might have affected the results. The control worms for the 48-hour 4 mm paraquat stress were also treated with FUdR. We have clarified this in the manuscript and noted that the presence of FUdR has the potential to alter gene expression.

__ Important: Please make clear how many replicates were performed for each experiment, and where relevant, how many worms were measured per replicate (e.g., stress survival and lifespan). __

We have added a spreadsheet (Table S6) to include the number of replicates and number of worms per replicate for all experiments.__

For 2-way ANOVA analyses, please specify p values of both main factors as well as interaction terms and posthoc analyses where relevant.

__

We have included these additional details from our statistical analyses in Table S6.

__ In the second paragraph of the introduction, I suggest broadening slightly the description of why normal mitochondrial function is required for ATFS-1 important and degradation, because this helps the reader understand that any one of many perturbations to mitochondrial function (decreased bioenergetics, membrane potential, protein degradation, protein import; increased ROS; etc.) could prevent or reduce ATFS-1 import and degradation.

__

We have added these additional factors that might prevent ATFS-1 import and degradation in paragraph one of our introduction and broadened the description in paragraph two.

__ For Figure 1: The authors present their choice of genes to analyze as if, and interpret their results assuming, that each of these gene is ONLY regulated by the indicated stress response pathways. I think this is very unlikely. For example: is it certain that sod-3 and trx-2 are not also skn-1 regulated? How is "antioxidant" distinguished from the skn-1 pathway? Further clouding the water is the likelihood that nuo-6 and atfs-1 manipulations alter physiology in such a way that there are secondary/indirect stress pathways activated (for example: the authors show that ATFS-1 overexpression shortens lifespan. Perhaps this is why it appears that ATFS-1 overexpression also appears to cause a strong, although variable, upregulation of the cytosolic UPR?). The likelihood (in my opinion) that these genes are in fact regulated by more than one type of response element, and that the manipulations used to study these relationships have pleiotropic effects, do not invalidate the general conclusion that these pathways interact-but they do mean that the results should be discussed with more caveats regarding HOW they interact.

__

These are excellent points. The genes that we selected for Figure 1 are the genetic targets that in our reading of the literature have been most often used to represent a particular stress response pathway. We have added references to justify the association of each gene with the indicated stress response pathway. We have also noted that in at least some cases the stress response genes that have been typically used to represent a specific pathway can be activated by multiple pathways. We agree that the selection of genes for Figure 1 is not a comprehensive approach, and that it is possible that if we chose a different gene from each of these pathways, the results might be different. We have updated our manuscript to specifically note these limitations. To avoid these limitations, we examined the overlap between all of the genes significantly upregulated by ATFS-1 activation and all of the genes significantly upregulated by the different stress response pathways in Figure 2. In addition, to gain a better understanding of the overlap between these different stress response pathways globally, we have compared gene expression between each of the stress response pathways studied in Figure S1.

__Figure 1 also illustrates why a more detailed description of sample size and statistical analysis should be provided. What was the "n"? What were the main effects and interaction terms of each 2-way ANOVA? The design is not full factorial and therefore does not permit a simple 2-way ANOVA (i.e., not all condition combinations are performed)-which responses precisely were compared to which? Were 2 2-way ANOVAs performed per mRNA?

__

For Figure 1 we used a one-way ANOVA to compare all of the groups to wild-type with a Bonferroni’s Multiple Comparison post-hoc test. We have updated the manuscript to include the sample size and statistical details in Table S6.

__ The work shown in Figure 2 is a very nice way to leverage previous data to further explore this idea of cross-talk. I would suggest including a bit more meta-data in the supplemental data files related to each dataset. For example, what lifestages were used (were they all young adult?), was FUDR used, etc.

__

We have added these details to Table S3, which includes the lists of target genes from each stress response pathway.

__ However, again, I don't understand how the authors can reach this conclusion: "Combined, this indicates that activation of ATFS-1 is sufficient to upregulate genes in multiple stress response pathways." (lines 152-153 but similar phrasing occurs multiple times) Could it not simply be that one form of cellular stress often eventually triggers broader cellular dysfunction, thus activating other cell stress pathways? Ie-how do we know whether these genes are directly regulated by atfs-1 binding regulatory elements, as implied by this phrasing?

__

This conclusion is derived from our data showing that constitutively active ATFS-1 mutants have significant upregulation of target genes from multiple stress response pathways (Figure 2). As the worms in those experiments were not exposed to stress, we don’t have reason to believe that they are experiencing cellular stress or dysfunction. We think it is more plausible that activation of ATFS-1, which normally occurs in response to stress, leads to the activation of other stress response pathways, either directly or indirectly, and that these pathways are recruited to help regain mitochondrial homeostasis. We don’t mean to imply that activated ATFS-1 binds directly to the target genes of other stress response pathways. We have clarified this in the revised manuscript.

__ The stress response experiments are very nicely done and very interesting. I appreciate that the authors did not shy away from describing counterintuitive results (eg et15 mutants showing increased sensitivity to chronic oxidative stress), and think that these results should also be briefly considered in the Discussion.

__

We have updated our manuscript to discuss the observation that atfs-1(et15) mutants have increased sensitivity to chronic oxidative stress.

__

__

__ __

__Figure 3: please report ANOVA interaction terms-these are what tell whether the inductions are in fact dependent on atfs-1 (not the post-hoc analyses). Again, it also appears that in some cases, there is an upregulation of certain genes with atfs-1 knockdown-please report all p-values (because there will be many, I recommend a supplemental table with all main and interaction and posthoc analyses). Again, the "n" also needs to be specified.

__

We have added Table S6 to include all of these statistical details.

__ Figure 4 A-C appear to be lacking error bars? Please add. Perhaps relatedly-the effect size for 4A looks much larger than for 4B, but this does not come across in the text.

__

We have added error bars to Figure 4A-C. We think the difference in effect size might result from the fact that 4A is an acute assay and 4B is a chronic assay. We speculate that the negative effect of the et15 and et17 mutations on lifespan might be a stronger factor in the chronic assay. We have updated the text to comment on the relative effect sizes.

__ For Figures 4 and 6, please indicate sample size-number of independent experimental replicates, and number of worms per replicate (or range per replicate).

__

We have added the number of replicates and sample size in Table S6.

__ Lines 224-225 re. sod-2 mutants: these may also act by decreasing ROS signaling (less conversion of superoxide anon to hydrogen peroxide); also, why would this strain not be considered another long-lived mitochondrial mutant (like clk-1, isp-1 and nuo-6, to which it is contrasted)?

__

We think the sod-2 mutation extends lifespan by increasing ROS signaling, as treatment with antioxidants decreases their lifespan. The increased superoxide from the loss of sod-2 may be converted to H2O2 by sod-3 or sod-1, which are also present in the mitochondria. We don’t include sod-2 with the mitochondrial mutants because the mutation does not directly impact the mitochondrial electron transport chain, but may do so secondarily due to elevated ROS.

__ The confirmation that atfs-1 overexpressing strains are short-lived is very interesting. However, I think this statement "Combined, this indicates that ATFS-1 does not play a major role in lifespan determination in a wild-type background despite having an important role in stress resistance." (lines 265-267 and similar in several places throughout the Discussion, eg line 279) should be altered to indicate that this was observed under controlled laboratory conditions. Eg, "...this indicates that ATFS-1 does not play a major role in lifespan determination in a wild-type background under optimized laboratory conditions..."

__

This is an interesting point. It is possible that constitutive activation of ATFS-1 may be beneficial for lifespan in an environment where worms are exposed to external stressors. We have noted that our lifespan results were obtained under lab conditions, which are believed to be relatively unstressful.

__

__

__ __

__Discussion: consider adding in a consideration of dose-response, both of knockdown of mitochondrial genes (eg, k/d of many mitochondrial genes promotes lifespan at low levels, but decreases lifespan with greater knockdown) and of stressors (chemicals, heat, etc; for chemicals, at the least, dose-response is very important, with low levels not infrequently triggering apparently beneficial stress responses, and higher levels causing toxicity).

__

It is possible that the magnitude of ATFS-1 activation will impact its effect on stress resistance and lifespan. Perhaps, a milder activation of ATFS-1 will be more beneficial with respect to lifespan. The degree of ATFS-1 activation may also account for differences that we observe between atfs-1(et15) and atfs-1(et17) mutants. atfs-1(et15) has more differentially expressed genes than atfs-1(et17) suggesting the possibility that it has more ATFS-1 activation. We have updated our manuscript to include these points.

__ Section beginning on line 384 "ATFS-1 upregulates target genes of multiple stress response pathways"-again, please revise to make clear that this work does not demonstrate direct regulation.

__

We have clarified that our results don’t demonstrate direct regulation. In addition, we have examined published ChIP-seq datasets to determine if there is evidence of direct regulation.

__ It seems to me that our reviews are in pretty good agreement. I agree with Reviewers 1 and 3 where they commented on things that I did not. While I did not consider the manuscripts as overlapping in the sense of being redundant, I very much like Reviewer 1's suggestion that they be published back to back and that the Discussion of each incorporate consideration of the Results of the other.

__According to this suggestion, we have arranged for these papers to be considered for publication at the same time in EMBO Reports and Life Science Alliance. We have updated the discussions of both manuscripts to incorporate the findings of the other manuscript.

__ Reviewer #3:

**Major comments**

1.The authors mention that activation of the UPRmt by nuo-6 mutants or atfs-1(gf) do not activate the ER UPR or cyto-UPR gene expression targets (lines 111-113). However, they also find that atfs-1(gf) animals have 25% overlap with the ER UPR pathway (line 146-147). Is 25% overlap not substantial?

__

The genes that we are referring to in lines 111-113 are the genetic targets that in our reading of the literature have been most often used to represent the ER-UPR or Cyto-UPR. This is not a comprehensive approach, and it is possible that if we chose a different gene from each of these pathways, the result might be different. We have updated our manuscript to include this limitation. To avoid this limitation, we examined the overlap between all of the genes significantly upregulated by ATFS-1 activation and all of the genes significantly upregulated by the ER-UPR or Cyto-UPR in Figure 2. In both cases, we find the overlap is significant, indicating that activation of ATFS-1 leads to activation of ER-UPR and Cyto-UPR target genes.

__

__

__ __

__To determine whether ATFS-1 mediates any protective effect during ER stress, authors should test atfs-1(gf) and atfs-1(lf) animals' resistance to ER stress.

__

To examine the effect of ATFS-1 on resistance to ER stress, we exposed wild-type, atfs-1(gk3094), atfs-1(et15) and atfs-1(et17) worms to 50 µM tunicamycin beginning at young adulthood and monitor survival daily. We found that both constitutively active atfs-1 mutants, et15 and et17, have increased resistance to ER stress compared to wild-type worms, while atfs-1 deletion mutants have a similar survival to wild-type. We have added this new data to Figure 4.

__ Authors should comment on the difference in outcomes with atfs-1(et17) and atfs-1(et15) animals to chronic oxidative stress (line 184-187).

__

We have updated our manuscript to discuss the observation that atfs-1(et15) mutants have increased sensitivity to chronic oxidative stress.

__ Lines 258-260. The authors should make clear in this section that a previous study had already measured lifespans of atfs-1(gf) animals and found that it was reduced (PMID 24662282). Also, an elaboration on why this experiment was repeated would be warranted.

__

We have referenced the lifespan results from this previous study in our introduction (line 53-54, Bennett et al), in our results section (lines 342-343; “which is consistent with a previous study finding shortened lifespan in atfs-1(et17) and atfs-1(et18) worms”) and in our discussion (lines 429-431; “as well as previous results using constitutively active atfs-1 mutants (et17 and et18) show that constitutive activation of ATFS-1 in wild-type worms results in decreased lifespan”). The reasons that we repeated this result are (1) because the lifespan of the atfs-1(et15) mutant had not been measured and this was the allele that we used in our paper; and (2) because the shortened lifespan is a surprising result given the beneficial effect of ATFS-1 on stress resistance, we thought it was important to repeat this experiment under the same conditions that we measured stress resistance.

__ The authors find that atfs-1(gk3094) animals lived longer during infection with PA14 (line 208-211). Another study found that atfs-1(gk3094) animals died faster on PA14 (PMID 28283579), which should be mentioned and commented on.

__

We have added this finding to our discussion. We have also compared the protocols used by Jeong et al. (who observed decreased survival in atfs-1(gk3094) deletion mutants), Pellegrino et al. (who observed wild-type survival in atfs-1(tm4919) deletion mutants and our manuscript (in which we observed slightly increased survival in atfs-1(gk3094) deletion mutants), to see which parameters might account for the observed differences.

__**Minor comments**

Line 38: "Inside the mitochondria, ATFS-1 is degraded by the Lon protease CLPP-1/CLP1". The phrasing suggests that CLPP-1/CLP1 is a Lon protease, when in fact they are independent proteases.

__

We have removed the word “Lon” to clarify this.

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Referee #2

Evidence, reproducibility and clarity

Summary:

The authors carried out experiments, and mine published datasets, to further characterize the role of the ATFS1 transcription factor in mediating survival and lifespan in laboratory or stressed conditions. The role of ATFS-1 was assessed by using a loss-of-function deletion and two constitutive gain-of function mutants in which the mitochondrial leader sequence is not functional, resulting in continual nuclear translocation. The effect of ATFS1 loss or constitutive activation was assessed in both wild-type and mutant (mitochondrial function and long-lived mutants) strains, and either under standard laboratory conditions or in the context of a variety of physical, chemical, and pathogen stressors. Constitutive ATFS-1 activation upregulated genes from a number of stress-response pathways, and the loss of atfs-1 blocked upregulation of some stress-response genes by a variety of exogenous stressors, with little or no effect on baseline expression of those genes. Loss of atfs-1 also increased sensitivity to many exogenous stressors (not all mitochondria-targeting), and overexpression was generally protective. However, overexpression also decreased lifespan in the absence of exogenous stressor.

Major comments:

• Are the key conclusions convincing? Mostly, assuming sample size was adequate (see below). The only major conclusion that I would qualify is "ATFS-1 serves a vital role in organismal survival of acute stresses through its ability to activate multiple stress response pathways"-the data, as presented, does not make clear whether ATFS-1 directly activates these pathways (ie, by binding response elements in genes in those pathways), or indirectly influences them by altering the physiology of the worm).
• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? No.
• Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation. No.
• Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments. N/A
• Are the data and the methods presented in such a way that they can be reproduced? Mostly; see below.
• Are the experiments adequately replicated and statistical analysis adequate? Unclear; see below.

Minor comments:

• Specific experimental issues that are easily addressable:

In abstract, consider broadening/re-wording "Gene expression changes resulting from the activation of the mitoUPR are mediated by the transcription factor ATFS-1/ATF-5." Because a naïve reader may understand this to suggest that ATFS-1 is activated only by mitochondrial protein misfolding. Please indicate whether strains were outcrossed, and how often.

How was "young adult" defined? Were worms synchronized, and if so, how?

For the gene expression experiments, do I understand correctly that FUDR was used only for oxidative stress and adult day 2 experiments? Please clarify. Important: Please make clear how many replicates were performed for each experiment, and where relevant, how many worms were measured per replicate (e.g., stress survival and lifespan).

For 2-way ANOVA analyses, please specify p values of both main factors as well as interaction terms and posthoc analyses where relevant. - Are prior studies referenced appropriately? Yes. - Are the text and figures clear and accurate? Yes. - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Yes:

In the second paragraph of the introduction, I suggest broadening slightly the description of why normal mitochondrial function is required for ATFS-1 important and degradation, because this helps the reader understand that any one of many perturbations to mitochondrial function (decreased bioenergetics, membrane potential, protein degradation, protein import; increased ROS; etc.) could prevent or reduce ATFS-1 import and degradation.

For Figure 1: The authors present their choice of genes to analyze as if, and interpret their results assuming, that each of these gene is ONLY regulated by the indicated stress response pathways. I think this is very unlikely. For example: is it certain that sod-3 and trx-2 are not also skn-1 regulated? How is "antioxidant" distinguished from the skn-1 pathway? Further clouding the water is the likelihood that nuo-6 and atfs-1 manipulations alter physiology in such a way that there are secondary/indirect stress pathways activated (for example: the authors show that ATFS-1 overexpression shortens lifespan. Perhaps this is why it appears that ATFS-1 overexpression also appears to cause a strong, although variable, upregulation of the cytosolic UPR?). The likelihood (in my opinion) that these genes are in fact regulated by more than one type of response element, and that the manipulations used to study these relationships have pleiotropic effects, do not invalidate the general conclusion that these pathways interact-but they do mean that the results should be discussed with more caveats regarding HOW they interact.

Figure 1 also illustrates why a more detailed description of sample size and statistical analysis should be provided. What was the "n"? What were the main effects and interaction terms of each 2-way ANOVA? The design is not full factorial and therefore does not permit a simple 2-way ANOVA (i.e., not all condition combinations are performed)-which responses precisely were compared to which? Were 2 2-way ANOVAs performed per mRNA?

The work shown in Figure 2 is a very nice way to leverage previous data to further explore this idea of cross-talk. I would suggest including a bit more meta-data in the supplemental data files related to each dataset. For example, what lifestages were used (were they all young adult?), was FUDR used, etc.

However, again, I don't understand how the authors can reach this conclusion: "Combined, this indicates that activation of ATFS-1 is sufficient to upregulate genes in multiple stress response pathways." (lines 152-153 but similar phrasing occurs multiple times) Could it not simply be that one form of cellular stress often eventually triggers broader cellular dysfunction, thus activating other cell stress pathways? Ie-how do we know whether these genes are directly regulated by atfs-1 binding regulatory elements, as implied by this phrasing?

The stress response experiments are very nicely done and very interesting. I appreciate that the authors did not shy away from describing counterintuitive results (eg et15 mutants showing increased sensitivity to chronic oxidative stress), and think that these results should also be briefly considered in the Discussion.

Figure 3: please report ANOVA interaction terms-these are what tell whether the inductions are in fact dependent on atfs-1 (not the post-hoc analyses). Again, it also appears that in some cases, there is an upregulation of certain genes with atfs-1 knockdown-please report all p-values (because there will be many, I recommend a supplemental table with all main and interaction and posthoc analyses). Again, the "n" also needs to be specified.

Figure 4 A-C appear to be lacking error bars? Please add. Perhaps relatedly-the effect size for 4A looks much larger than for 4B, but this does not come across in the text.

For Figures 4 and 6, please indicate sample size-number of independent experimental replicates, and number of worms per replicate (or range per replicate).

Lines 224-225 re. sod-2 mutants: these may also act by decreasing ROS signaling (less conversion of superoxide anon to hydrogen peroxide); also, why would this strain not be considered another long-lived mitochondrial mutant (like clk-1, isp-1 and nuo-6, to which it is contrasted)?

The confirmation that atfs-1 overexpressing strains are short-lived is very interesting. However, I think this statement "Combined, this indicates that ATFS-1 does not play a major role in lifespan determination in a wild-type background despite having an important role in stress resistance." (lines 265-267 and similar in several places throughout the Discussion, eg line 279) should be altered to indicate that this was observed under controlled laboratory conditions. Eg, "...this indicates that ATFS-1 does not play a major role in lifespan determination in a wild-type background under optimized laboratory conditions..."

Discussion: consider adding in a consideration of dose-response, both of knockdown of mitochondrial genes (eg, k/d of many mitochondrial genes promotes lifespan at low levels, but decreases lifespan with greater knockdown) and of stressors (chemicals, heat, etc; for chemicals, at the least, dose-response is very important, with low levels not infrequently triggering apparently beneficial stress responses, and higher levels causing toxicity).

Section beginning on line 384 "ATFS-1 upregulates target genes of multiple stress response pathways"-again, please revise to make clear that this work does not demonstrate direct regulation.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. The mitoUPR has generally been viewed and tested as an isolated mitochondrial stress-specific response; the authors have built upon previous work to convincingly show that it is integrated with a variety of other stress response pathways. This is an important contribution to the field.
• Place the work in the context of the existing literature (provide references, where appropriate). The authors have done a nice job of this in their discussion.
• State what audience might be interested in and influenced by the reported findings. Researchers interested in stress response in general, and mitochondrial homeostasis and stress response in particular, as well as the relation of these to lifespan.
• Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate. Mitochondrial response to exogenous stressors, particularly pollutants.

Referees cross-commenting

It seems to me that our reviews are in pretty good agreement. I agree with Reviewers 1 and 3 where they commented on things that I did not. While I did not consider the manuscripts as overlapping in the sense of being redundant, I very much like Reviewer 1's suggestion that they be published back to back and that the Discussion of each incorporate consideration of the Results of the other.

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Reply to the reviewers

Reviewer comments:

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

In this paper, the authors examine the relationship between the transcription factor Ribbon, its ribosomal protein gene (RPG) targets, and cell growth during the process of salivary gland tubulogenesis in the Drosophila embryo. This study builds upon previous work they published in 2016 (Loganathan et al., 2016). While the previous study identified RPGs as potential targets of Ribbon from ChIP-Seq analysis, they did not delve into the role of these targets in salivary gland morphogenesis. Here, the authors demonstrate that mutation of ribbon results in decreased cell volumes via immunostaining and image analysis. They identify and confirm RPGs as ribbon transcriptional targets using ChIP-SEQ, Microarray data, in situ hybridization, and qRT-PCR. They analyze these targets in an effort to identify a Rib consensus binding sites by MEME and find that Rib binding is not specific using EMSA. They suggest specificity arises from association with transcriptional cofactors. Binding with cofactors was confirmed by CO-IP and in vivo RNAi experiments demonstrated the requirement of these cofactors in mediating changes in cell volume during salivary gland tubulogenesis. They demonstrate that Ribbon regulation of cell growth via transcription of RPGs is not a universal mechanism for Ribbon function, as Ribbon regulates transcription of other genes in the context of tracheal development.

**Major comments:**

Results of all experiments are conclusive, and significant numbers of samples were noted for most figure panels. For a few panels the sample number/number of replicates was not noted, and it is recommended that the authors add this information (Figure 1F; 5B,C; 7B).

Additional experiments are not needed to support the conclusions presented in this work. The data and methods are presented clearly and the statistical analyses performed were appropriate.

In regard to microarray data, Figure 4E shows fold change as log2 values, but it is unclear if this is the case for Table S2. This should be clarified. The authors note in the text on page 7 that few targets show a greater than 1.5-fold change. Based on Figure 4E, this is a log2 value, and should be specified as such.

As the Rib antibody was generated in this study, it would be helpful to include data illustrating a confirmation of antibody specificity. This could include Rib antibody staining on rib mutant embryos, or showing a lack of band for ribbon in ribbon mutants on a Western blot. If the specificity has been published elsewhere, please add a reference.

**Minor Comments:**

As the microarray data was previously published in Loganathan et al 2016, as mentioned in the results section, this citation should also be included in the Methods section describing the Microarray data.

In the discussion section on page 15, a list of factors in the gene network are listed. What is viz.?

Reviewer #1 (Significance (Required)):

•As described in the introduction, the role of cell growth during embryonic tissue morphogenesis is a relatively unexplored topic. The authors point out that most previous studies describing regulation of tissue growth have focused on the role of mitosis and increased polyploidy, as in the gut (https://doi.org/10.1016/S0925-4773(00)00512-8 ), as primary mechanisms. In the case of the salivary gland, only a single endocycle occurs during embryogenesis and cells are post-mitotic, suggesting another mechanism is at play. This study identifies Ribbon as a mediator of cell growth and demonstrates that Ribbon mediates this function through transcriptional regulation of RPGs. In addition, they identify Ribbon cofactors that are important for salivary gland cell growth and tissue morphogenesis. Interestingly, they find that this mechanism for cell growth may be tissue specific, as Ribbon appears to regulate different genes in the trachea.

•This work has implications for the regulation of cell growth in other tissues and organisms and would be of broad interest to those studying organ development.

•In order to contextualize my review, I am a developmental biologist that works with Drosophila.

**Referees cross-commenting**

In regard to the comments by reviewer #2: I agree that point # 2 should be addressed to more thoroughly describe the method, but as the authors have looked at DNA Amplification at a time point following the normal endocycle, which occurs at stage 12, and DNA content is not significantly different, I don't think analysis of earlier stages would influence their conclusions.

Given that the authors do include some RNAi data for RPGs and Trf2, it would enhance the paper further to include M1BP and Dref RNAi data if quality reagents are available as described in point 5. Point 6 can be easily addressed. In regard to point 8, the effects of rib overexpression alone would be interesting to see given the ability of this construct to rescue the phenotype.

While I think points 3 and 7 are excellent ideas for a follow up study, I think they are outside of the scope of this paper. I do not view point 4 as essential to this study, as the study focuses on the regulation of transcription of the RPGs by Rib.

In regard to the comments by reviewer #3, I agree that points 1 and 2 should be addressed. It would be extremely difficult to address point #3 by dissecting out the tissue, but it could be addressed via further explanation in the text, as could point #4. I don't think minor points 4-6 need to be addressed, but the minor points 1-3 should addressed to improve the paper. For minor point #3, I would suggest the number of genes be included in Supplementary Table 1.

As reviewer #1, I think my comments should be addressed to improve the quality and clarity of the paper.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

This paper reported a role for the BTB/POZ-domain transcription factor rib in mediating early cell growth of embryonic salivary gland (SG) cells. the authors show that during tubulogenesis of the salivary glands, rib binds the transcription start site of almost all SG-expressed ribosomal protein gene (RPG) and promotes their transcription, thus providing a material foundation for cell growth. Interestingly, in embryo trachea cells, rib targets do not include RPGs, which indicates that rib may use different mechanisms to regulate cell growth of different organs. In general, this is a well-written, well designed research article with many conclusions well-supported by experimental evidence. Listed below are a few issues (mostly minor/unessential) for the authors to consider.

**Major comments:**

1.Although in Figure 1G, the nucleus size is indistinct in rib mutant and wt cells at stage 15 and 16, Figure 1C appeared to look like that the rib mutant nuclei at stage 11, 13 and 14 are significantly smaller than those in wild type cells. The authors need to make sure that the rib phenotype has nothing to do with DNA amplification.

2.Please describe the details on calculating DNA volume by DAPI staining in the method session.

3.The authors have demonstrated weak DNA binding ability of Rib, and physical interactions between Rib with the known regulators of RPG transcription (Trf2, M1BP, and Dref), but what is the functional relationships between Rib and the known RPG regulators? e.g., does Rib function to promote DNA binding and transcriptional activity of Trf2, M1BP, and Dref, or vice versa?

4.To confirm the rib function on RPG translation, it is recommended to examine ribosomal proteins by western, and comparing the total protein content would also be helpful.

5.As Trf2, M1BP and Dref are physically interacted with Rib, it would be helpful to determine Whether M1BP and Dref knockdown can phenocopy the cell growth deficit observed in rib mutant SGs.

6.Page12, paragraph 3, "Thus, despite the shared requirement for Rib in embryonic cell growth of both tubular organs, Rib-dependent growth in the trachea is likely through regulation of alternative growth-promoting factors." Please list the potential growth-promoting factors targeted by Rib according to the Chip-seq data, if possible.

7.It would be interesting to determine whether rib mutation differently affect the secretory function of salivary gland at embryo, larva, pupa or adult stage.

8.Does Rib overexpression have any effects to SG development? Considering the authors adopted GAL4-UAS system to rescue Rib under Rib-KO, it would be interesting to see if Rib overexpression could cause an opposite overgrowth phenotype.

Reviewer #2 (Significance (Required)):

This paper discovered a new mechanism underlying organ-specific cell growth regulation during a specific time-window of animal development, which should be of interest to the field of cell and developmental biology.

Drosophila genetics; Developmental biology

**Referees cross-commenting**

I agree with all the other referees that the comments raised by reviewer #1 should be addressed entirely.

In regard to the comments by reviewer #3, all of the 4 major points are excellent and should be addressed, but it is okay to address points #3 and 4 by simple explanation or re-wording. I find the minor point #6 is nice to have but not essential, the rest should be addressed.

In case of my comments (reviewer 2), points #1,2,5,8 should be addressed, others are nice to have.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

In the manuscript "The Ribb-osome: Ribbon boosts ribosomal protein gene expression to coordinate organ form and function" the authors show evidence that Ribbon mediates early cell growth in Drosophila embryonic salivary gland through direct interaction with ribosomal protein genes. The manuscript is well written while presenting novel and solid data. The data could be strengthened by some further analysis and clarification, but none of the issues raised represent major flaws.

**Key points:**

1.Cell segmentations: The way the cell segmentations / volume quantifications are presented it is impossible to judge their quality. The authors should provide the extracted geometries as Supplementary Data. The methods could be clearer on how the segmentations for cell and DNA volume were done; were the surfaces done manually, were there any image preprocessing steps etc.? In Figure 7C, it is not clear from the images whether cells or nuclei were segmented. Also, it would strengthen the work if the authors analysed the cell shapes (in particular cell height, and apical cell shape bias), considering that they mention it to be different in the Rib mutant. In addition, it would add to the manuscript if the authors could quantify the volume of the luminal space, of the epithelial layer in wt and mutant, and the bias in tube outgrowth.

2.The authors show nicely that the rib mutants have a smaller overall cell size, can this be the reason why the secretory tube in figure is smaller? In addition, if the overall size of the mutant and the WT is the same as suggested in figure 1H then why does the mutant larvae in figure 1f appear so much smaller than the WT in the same panel?

3.In figure 4f the authors see 4 out of 7 RPGs been significantly down-regulated, do they have an explanation for that? Why are not all 7 tested RPGs significantly down-regulated? Can it be that the results will be significantly improved by dissecting the tissue of interest instead of using whole embryos? Finally with what criteria were these 7 genes selected?

4.The authors state in their manuscript the limitations of the chip-seq and the fact that the 11 unbound RPGs are essentially a technical artifact. I suggest that the authors either perform ChIP on some of these RPGs to prove their point or that they ton down their statements about chip-seq limitations and Rib binding all SG-expressed RPGs

**Minor points**

The authors need to clarify in the text what is early and late stage of tubulogenisis.

In figure 1c the Mipp1 staining is of low quality and although the white lines help the reader on where to focus, noise vs signal is almost indistinguishable. Furthermore, the authors claim that they only take under consideration SG cells that show uniform membrane staining but Figure 1c does not show such uniform staining.

Figure 1d needs the addition of statistical analysis WT vs rib mutant st12 look very similar.

In their ChIP-seq data the authors identify 436 peaks that correspond to 413 genes. It is worth to add a pie chart depicting how many of those 413 are RPGs and how may are non-ribosomal.

Throughout the manuscript the authors exhibit nicely the effects of rib mutants. What happens to the tested genes in panel 4f when rib is overexpressed?

RPls are known to be involved in size regulation. If the authors use another driver than fkh to express Rib, Rpl19 etc will they still see similar phenotypes or not?

Figure 7b is hard to follow, the IP panels should be in agreement with the order that they appear in the text e.g., first experiment then controls

Reviewer #3 (Significance (Required)):

In the manuscript "The Ribb-osome: Ribbon boosts ribosomal protein gene expression to coordinate organ form and function" the authors show evidence that Ribbon mediates early cell growth in Drosophila embryonic salivary gland through direct interaction with ribosomal protein genes. As I am only vaguely familiar with the field, I would leave it to someone who is closer to judge the advance and relevance. But with the additional quantifications, the paper should be of interest more generally to developmental biologists who are interested in tubulogenesis, and if the authors make the 3D cell geometries available, the work should also be of interest to computational modellers with an interest in epithelial organization as segmented 3D cell geometries are still rare.

**Referees cross commenting**

Looking at all 3 referee reports, I find all points made by referee 1 either essential and/or easy to fix. As such, I would insist on all points made.

With regard to referee 2, I see points 1,5,8 as essential, and point 2 is too easy to do to not request it. The others I would consider nice-to-have, but not essential.

In case of my own report, I would insist on points 1 & 2. Among the minor points, points 4 & 6 are NOT essential. The others are either important or easy enough to fix.

I look forward to the views of my colleagues.

Our response to reviewer comments

We thank the reviewers for their very positive comments regarding the importance of this paper and for the constructive feedback they have provided. Indeed, we would be delighted to address every suggestion raised, but since we would also like to have this work published in a timely manner, it is quite helpful to have consensus among the three reviewers regarding which changes and experiments are the most important to include. Since all three reviewers felt it important to address all of the comments from Reviewer #1, we will do so. For the comments raised by reviewers #2 and #3, we will follow the consensus opinion and address those comments by changes in the text or by including more experiments. In this revision plan, we also address the comments that were considered to be beyond the scope of the current study.

Points raised by Reviewer #1

Include N values for all the figure panels: We will provide sample number information for those panels currently missing that information: Figures 1F; 5B, C; and 7B.

Microarray fold-change clarification: We will clarify that we are reporting the fold-change values in Table S2. As is standard with Volcano plots for reporting microarray data, Figure 4E is plotted as Log2 data.

Antibody validation: We will provide a supplemental figure with information about the Rib antiserum and its specificity.

Add citation regarding the microarray data: We will add the citation referring to the microarray data to the Methods section.

Uncommon word usage pg 15: We will remove “viz.”—contraction of a Latin phrase “videre licet” to mean “namely” or “specifically”—from the discussion of factors in the gene network, since it was clearly distracting.

Points raised by Reviewer #2

Appearance of Nuclei and Calculation of DNA volume: The rib mutant nuclei shown in Fig. 1C depict CrebA staining and were used only for identification of SG secretory cells – we did not measure nuclear volume in these samples. To eliminate any potential confusion, we have re-labelled the last column “3D cell volume”. All of the calculations of nuclear size (as a measure of DNA amplification) were carried out with DAPI-staining as shown In Fig 1G, which revealed no difference between WT and rib mutant SG secretory cells. Measurement of entire nuclear volume is critical, since, in any single focal plane, how much of the nucleus is captured varies. We will provide information detailing how DNA volume was obtained in the methods section.

SG cell size phenotypes of M1BP and Dref RNAi Knockdowns: We agree with the reviewers that determining if M1BP and Dref SG-specific RNAi also phenocopy the cell growth deficit observed in the rib mutant SGs is a meaningful experiment and could strengthen our conclusions. We will, therefore, perform this experiment. It should be noted, however, that whereas rib and Trf2 do not have significant levels of maternal mRNA or protein, both M1BP and Dref have high levels of both [based on ModEncode data; Flybase]. Thus, it may be challenging to deplete these genes with only SG driven expression of the RNAi constructs.

List of potential Rib-dependent growth promoting factors in the trachea: In the revised version, we provide the list of candidate growth genes bound by Rib from the tracheal Chip-Seq data as requested by reviewer #2 (and agreed upon by reviewer #1 as important) in the supplement.

Effects of Rib overexpression on SG cell growth: All of the reviewers agree that testing for a SG secretory cell over-growth phenotype with Rib overexpression is worthwhile and we will do this experiment. Nonetheless, we recognize that we may not see overgrowth phenotypes based on a few observations. Our ChIP-Seq data indicate that Rib binds neither the promoters of ribosomal RNAs [rRNAs; the other essential component of ribosomes] nor the promoters of known rRNA transcription factors. Based on a study from another group, it seems likely that Myc upregulates rRNA expression (Grewal et al., 2005). Correspondingly, myc is transcriptionally upregulated in the embryonic SG (supplemental panel 7C) and myc expression in the SG is independent of rib (i.e. Rib does not bind the myc gene based on the SG ChIP-Seq and myc levels in the embryonic SG do not change in rib null embryos based on microarray and whole mount in situs). Also based on ChIP-Seq, Rib binds its own promoter and, based on qRT-PCR experiments, represses its own expression (Loganathan et al., 2016). Thus, over-expression of Rib with GAL4:UAS driven expression may reduce rib transcription from the endogenous locus. Nonetheless, this experiment is still worth doing.

Points raised by Reviewer #3

Information on cell segmentations: In the revised manuscript, we will provide sample 3D views of cell volume quantifications as movie files. In the methods section, we will also make it clear that the surfaces were manually segmented and that no image preprocessing steps were performed. We will also provide the excel spread sheets on size calculations in a supplement. We will provide information in the legend for figure 7 that whole secretory cells were segmented for the calculations done for panel C. The information on cell shapes, apical membrane dynamics, and luminal volumes (including the assessment of developmental dynamics of tube elongation based on live-imaging construction of computational elastic and analytical viscoelastic models) has been presented in previous publications from our lab (Cheshire et al., 2008; Loganathan et al., 2016) and from work in other labs (Blake et al., 1998). We will include this information in the revised discussion and will include the appropriate citations.

Panel 1F and comment on the apparent smaller size of the rib mutant shown: rib mutant embryos show characteristic head invagination defects along with amioserosa and dorsal closure defects [Bradley and Andrew, 2001]. The partial embryo image in Panel 1F captures the head invagination defect making the embryo appear smaller. We will include images of whole embryos in the revised version to clarify that whole embryo volumes of rib mutants are comparable to WT for the representations shown in Fig. 1F.

Clarify early vs. late Tubulogenesis: Early SGs are stage 11, 12 – when the SG cells are internalizing. Late SGs are stages 13 – 16, when the glands are fully internalized. We will clarify this in the figure legend.

Statistics on Panel 1D: We will perform statistical analysis of growth profiles shown in Fig 1D as suggested by the reviewer and include the results in the figure or figure legend.

Pie-chart for RPG fraction: Given how crowded the figures currently are, instead of providing pie charts, we simply provide the fraction of the bound genes that are RP genes in the text. Using our set cut-off of 4.0: 12.9% of genes bound by Rib (with both drivers) were RP genes. Using the IDR platform for peak calling, 12.8% of bound genes were RP genes. In Fig 4A, we also include genes above the cut-off with one GAL4 driver, but not the other, as described in the legend.

Effects of Rib Overexpression: As discussed earlier, we will perform this experiment (please also see our response to the last comment by reviewer #2)

Order of presentation of co-IP results in Panel 7B: As requested, we will reorder the IP results in Fig. 7B as suggested by the reviewer to present first the results from the experiments and then the results from controls in accord with how we discuss the data in the results section.

Testing the functional relationships between Rib and known RPG regulators: We will not determine if Rib promotes DNA binding and transcriptional activity of Trf2, M1BP, and Dref, as this experiment was considered to not be critical for this paper by any of the three reviewers.

Panel 4F and tissue-specific RT-qPCR: We agree that it would be ideal to have tissue-specific qRT-PCR, but it is not technically feasible to dissect out enough embryonic SGs for analysis (as acknowledged by Reviewer 1). In future studies, we do plan to get that kind of information from single cell RNA sequencing (scRNA-Seq) of WT and rib mutant embryos, but there are a few hurdles to overcome before those experiments. In selecting the RP genes for qRT-PCR, we chose sample RpL and RpS genes, making sure to include at least one gene (RpS9) that was “not bound” by Rib based on ChIP-Seq criteria.

Determine Rib function on RPG translation: We will not examine levels of RP proteins by Western since this experiment was deemed be unnecessary for the current study by the three reviewers.

Effects of rib on the secretory function of the SG at the embryo, larva, pupa, or adult stage: We agree with the reviewer that these data would be interesting to have; as pointed out by reviewer #1, however, it’s a question for a future follow-up study.

Chip-Seq technical artifact / limitations: We don’t think we are incorrect in suggesting that the failure to detect Rib binding to all RP genes could be a technical artifact because of the following: (1) a direct examination of the binding tracts associated with every RP gene reveals a peak at/near the TSS. The values associated with those peaks do not always reach the cut-off, but when the peak values are lower than the cut-off, the signals in the flanking DNA are often also much lower than average (for details, see Supplemental Figure 1). (2) Among the RP genes whose expression went down significantly by qRT-PCR is RpS9 – an RP gene “not bound” by Rib, based on the cut-offs we followed.

Using another SG driver: We agree with reviewer #1 that the results obtained using the fkh-GAL4 driver for RNAi of RP regulators and RP genes are robust and sufficient to support the conclusion that Rib binds RPGs to regulate SG secretory cell size. Thus, we will not redo these experiments using another SG driver.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

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Reply to the reviewers

Manuscript number: RC-2023-02157

Corresponding author(s): Satish, Mishra

1. General Statements [optional]

We thank the editor and reviewers for their helpful comments. We have successfully addressed most of the comments. We are performing some additional experiments as suggested by the reviewers and will be included if considered further. We attempted to pulldown the S14 interacting partner using anti-mCherry antibody from S14-3XHA-mCherry transgenic sporozoites and then further tried to identify interactome using mass spectrometry but failed. So, accordingly, we have toned down the conclusion.

The point-by-point response to the reviewer’s comments is given as follows.

2. Description of the planned revisions

Reviewer #1:

Figure 1F You have not formally shown that this signal corresponds to palmitoylated S14. Could be heavy chain. Response: The possibility of a heavy chain is negligible because we have used sporozoite samples and probed it with an anti-rabbit antibody conjugated to HRP. Also, the size of the S14 bands does not correspond to heavy chain. However, we have toned down the conclusion. Currently, we are performing the depalmitoylation experiment, and data will be included in the next round of revision.

Reviewer #2

Line 149: To definitively state S14 is a membrane protein, biochemical assays proving such should be performed. (or perhaps genetic mutation of the predicted palmitoylation site?) Otherwise, this should be rephrased. Response: We are performing the depalmitoylation assay, and the data will be included during the second round of revision. However, we have rephrased the sentence in the current version of the manuscript.

Lines 257-258: for yeast 2-hybrid, the controls of expressing S14, GAP45 and MTIP together with control proteins where no interaction would be predicted are absent. Response: We are performing experiments with additional controls, and data will be included in the next round of revision.

Reviewer #3

Conclusions that S14 knockout does not impact the expression and organization of two surface proteins, CSP and TRAP, and two IMC rely on a qualitative analysis only. However, quantitative analysis to support their observations is missing. Response: We are quantifying the IFA images and data will be included in the next round of revision.

3. Description of the revisions that have already been incorporated in the transferred manuscript

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

Summary: The authors have identified a sporozoite gliding motility protein through bioinformatic analysis. From the main text I do not know how, or what bioinformatic analysis was performed, in order to focus on this protein which is called S14. The authors then go on to tag the protein, produce a KO and show its involvement in gliding motility. The KO shows that parasites lacking S14 fail to invade the mosquito salivary glands. This is due to a motility defect. Y2H and docking studies are used to define an interaction with MTIP and GAP45, two known components of the glideosome. Response: We identified this gene from the Kaiser et al., 2004 paper (DOI: 10.1046/j.1365-2958.2003.03909.x). The S14 was found to be highly upregulated in salivary gland sporozoites but lacked signal sequence and transmembrane domain. Next, we looked into other sporozoite proteins lacking signal sequence and transmembrane domain and found several gliding-associated proteins with similar properties. By using the guilt-by-association principle (DOI: 10.1186/gb-2009-10-4-104), we studied the following properties of existing glideosome components along with S14: (1) Classical pathway secretion using the signal peptide (SignalP, https://services.healthtech.dtu.dk/services/SignalP-5.0) (http://dx.doi.org/10.1016/j.jmb.2004.05.028). (2) Nonclassical pathway secretion (SecretomeP , https://services.healthtech.dtu.dk/services/SecretomeP-1.0/) (10.1093/protein/gzh037). (3) Presence of transmembrane domains (TMHMM , https://services.healthtech.dtu.dk/services/TMHMM-2.0/) (10.1006/jmbi.2000.4315). (4) Presence of a potential palmitoylation site (CSS-Palm, http://bioinformatics.lcd-ustc.org/css_palm) (Ren et al, 2008). This is a similar association prediction method as employed by the STRING database. However, mentioning that we identified a gliding motility protein by bioinformatic analysis was wrong, and we modified the sentence.

Major comments: The paper is sometimes hard to follow and lacks clarity. The reason: important information is omitted, or explained at the end of a section rather than at first mention; experimental details that are of essence need to be mentioned or explained in the main text; there is ample use of the word 'bioinformatic' without explaining what kind of analysis was performed in the main text. I cite from the abstract: 'In silico analysis of a novel protein, S14, which is uniquely upregulated in salivary gland sporozoites, suggested its association with glideosome-associated proteins.' I cite from the introduction: 'A study comparing transcriptome differences between sporozoites and merozoites using suppressive subtraction hybridization found several genes highly upregulated in sporozoites and named them 'S' genes (Kaiser et al, 2004). We narrowed it down to a candidate named S14, which lacked signal peptide and transmembrane domains.' From reading the main text, I do not know why Plasmodium berghei S14 was chosen in this manuscript. S14 is one of 25 transcripts identified by Kappe et al in Plasmodium yoelii (https://doi.org/10.1046/j.1365-2958.2003.03909.x) to be upregulated in sporozoites. The material and methods section does not explain either why S14 was chosen. Perhaps the authors could update Figure 2 from Kappe et al with the most recent annotations from plasmodb. Response: We have edited the manuscript for clarity and mentioned the name of the bioinformatic analysis performed. We chose S14 from Kaiser et al., 2004 (https://doi.org/10.1046/j.1365-2958.2003.03909.x) that identified transcripts in P. yoelii. We work on the rodent malaria parasite P .berghei and validated S14 transcripts by qPCR which showed its upregulation in sporozoites.

Rodent malaria parasites P. berghei and P. yoelii have been used extensively as models of human malaria. Both species have been widely used in studies on the biology of Plasmodium sporozoites and liver stages due to the availability of efficient reverse genetics technologies, and the ability to analyze these parasites throughout the life cycle stages have made these two species the preferred models for the analysis of Plasmodium gene function. A genetic screen and phenotype analysis were performed in P. berghei (DOI: 10.1016/j.cell.2017.06.030 and DOI: 10.1016/j.cell.2019.10.030) that makes in-depth characterization easier due to the availability of reagents and preliminary gene-phenotype like its dispensability in the blood. As suggested by this reviewer, we have updated the most recent annotations from PlasmoDB.

Reproducibility: None of the main Figures or Figure legends define ' N = '. For example I cite: 'The S14 KO clonal lines were first analyzed for asexual blood-stage propagation, and for this, 200 µl of iRBCs with 0.2% parasitemia was intravenously injected into a group of mice.' There are 2 mentions of 'N=' in the supplementary figures. I have not found any others.

I'm not sure what the convention is. Should unpublished data for this gene (PBANKA_0605900) found in pberghei.eu (a database for mutant berghei parasites) be cited? After all it confirms their findings.

The authors need to use more recent references for some of their statements; see some comments below. __Response: __We have mentioned N in the figures legends of the revised manuscript and also mentioned the unpublished data of RMGM. We have also added recent references in the revised manuscript.

Minor comments:

line 1-2 Add the Plasmodium species of this study.

Response: Added.

abstract Which species do you work with?

Response: We have mentioned P. berghei in the abstract of the revised manuscript.

29 mosquito salivary glands and human host hepatocytes

Response: Corrected.

30 to the glideosome, a protein complex containing [...]

Response: Corrected.

32-33 What kind of in silico analysis suggested S14 is part of the glideosome? S14 is not uniquely upregulated; there are other S-type genes identified by Kappe and Matuschewski. 25 I believe.

Response: Mentioning that in silico analysis suggested S14 is part of the glideosome was a wrong statement, and we have modified the sentence for clarity in the revised manuscript.

32 Please point out he species were S genes were identified. SGS of which species?

Response: The S genes were identified in the transcriptomic study of Plasmodium yoelii.

34 expression: change to transcription

Response: Changed.

39 What kind of in silico analysis was used here? and therefore malaria transmission

__Response: __In silico, protein-protein docking interaction analysis was used.

55 A single zygote transforms into a single ookinete, which establishes a single oocyst, which in turn can produce thousands of midgut sporozoites. Please correct the life cycle passage.

Response: Corrected. located or anchored in the IMC? And located between the IMC and plasma membrane?

Response: Glideosome is located between the plasma membrane and IMC, and the same has been corrected in the revised manuscript.

61-63 Refer to Table S1 and its contents here 64 Name the known GAPs. Response: Done.

65-67 Which transmembrane domain proteins? Please add more recent references than King 1988.

Response: We have added TRAP as a transmembrane domain protein and updated the reference.

71-72 TRAP was the first protein found to be ...

Response: Corrected.

74-76 Add additional, more recent references: for example search Frischknecht and TRAP

Response: Added.

76 S6 (TREP) is also [...]

Response: Done.

88 Some of these proteins are also expressed in ookinetes.

Response: Corrected.

89-91 The sentence needs a verb.

Response: Added.

88-96 Please add some more recent glideosome papers. After 2013.

Response: Added.

91 Why do you call it a peripheral protein?

Response: Because the GAP45 was detected at the periphery of the merozoite in P. falciparum. As there are no such reports in sporozoites hence we have removed peripheral in the revised manuscript.

91-93 There are more recent citations for GAP45 and GAP50. Response: We have added recent citations.

96 Insert a reference here.

Response: Added.

99 Please define the gliding-associated proteins. What are they? Aren't there papers on GAP40, 45 and 50? DOI: 10.1016/j.chom.2010.09.002

Response: Done.

99 .... What prompted you to identify a novel GAP? And why is S14 classified as a GAP?

Response: This was a wrong statement, which we removed in the revised manuscript.

99-102 What kind of bioinformatic study? Why was S14 chosen? Please outline how you ended up with S14. Any other proteins that came out of the bioinformatic screen from the list of S genes?

Response: We identified S14 from the Kaiser et al., 2004 paper and analyzed its properties using the “guilt-by-association” principle. The analysis showed that S14 had properties similar to GAP45 and MTIP. The S14 upregulation in sporozoites and its properties similar to known GAPs, we were prompted to study this gene's function.

How many proteins were identified in the screen for sporozoite upregulated proteins by Kappe and Matuschewski?

Response: 25 genes were identified in that paper, including the two characterized genes CSP and TRAP during that study.

102-103 Define the nonclassical secretion pathway. Please reference GAP45 and GAP50 data for the nonclassical pathway.

Response: When proteins are secreted out of the cytosol without predictable or known signal sequences or secretory motifs are classified as non-classically secreted proteins, and the pathway is called a non-classical protein secretory pathway. References: https://doi.org/10.1371/journal.pone.0125191; https://doi.org/10.1016/S0171-9335(99)80097-1; doi: 10.3389/fmicb.2016.00194

105 Please add P. berghei to the title, the abstract, the introduction.

Response: Added.

111 The results section does not outline what bioinformatic analysis was used

Response: The guilt-by-association principle was used, and it is outlined in the revised manuscript.

112-114 Please specify the exact number of upregulated in sporozoites genes. I think it was 25. And add the species the study was performed in. Why did you choose the Kappe study but not the uis genes from berghei?

Response: It was 25, and the species was P. yoellli. The domains of all 25 proteins are shown in Figure 2 of Kappe study. It intrigued us after having a glance at it. Later, we confirmed the upregulation of S14 transcripts in P. berghei sporozoites and chose to study the function of this gene.

114-115 How did you narrow it down to S14? The Kappe paper lists 25 S-type genes from P. yoelii.

Response: The domains of all 25 proteins are shown in the Kappe study. Two proteins, S14 and S15, lack signal sequence and transmembrane domain, which intrigued us after glancing at them. We chose S14 because its microarray induction is higher compared to S15.

118 Plasmodia is not the plural for a group of different Plasmodium species. Use: [...] conserved among Plasmodium spp.

Response: Corrected.

118-119 Which proteins did you analyze? And how did you analyze them? Where is the data for this analysis? Outline the amino acids that predict palmitoylation? The nonclassical pathway?

Response: The proteins we analyzed are given in Table S1. We analyzed them by the guilt-by-association principle. The data for this analysis is shown in Table S1. The amino acids predicted to be palmitoylated are C59 and C228 (S14), C5 (GAP45), C8 and C5 (MTIP). Non-classical pathway secretion was predicted by SecretomeP ( 10.1093/protein/gzh037).

119-122 Here: do you mean S14 has similar properties as GAP 45 and GAP50? Define the nonclassical pathway? How do you know S14 is in the IMC?

Response: The similar properties of S14 and GAP45 are Signal Peptide Prediction, Prediction of Non-classical pathway secretion, number of predicted transmembrane domains and prediction of Palmitoylation signal. GAP50 was wrongly mentioned here and has been removed from the revised manuscript.

When proteins are secreted out of the cytosol without predictable or known signal sequences or secretory motifs are classified as non-classically secreted proteins. The pathway is called a non-classical protein secretory pathway.

Our colocalization data of S14 with GAP45 and MTIP indicated that S14 is in the IMC.

122-123 Please reference the bioinformatic analysis plus URL that allows targeting to the IMC to be analyzed.

Response: All the URLs with references are given in the method section, lines 348-358 in the revised manuscript.

123-124 Please reference the URLs for TM, palmitoylation, and interactions analyses.

Response: All URLs with references are given in the method section, lines 348-358 in the revised manuscript.

125-127 How did you predict that S14 is secreted via the nonclassical pathway?

Response: We predicted non-classical pathway secretion of S14 using - SecretomeP (https://services.healthtech.dtu.dk/services/SecretomeP-1.0/) (10.1093/protein/gzh037).

128-130 Define the nonclassical pathway when it first appears in your manuscript.

The citation Moskes 2004 is not in the reference list

Response: The nonclassical pathway is defined in lines 105-107. The citation Moskes 2004 has been included in the revised manuscript.

132 Which membrane?

Response: Live S14-mCherry localization on the membrane does not differentiate between the outer membrane or IMC. Hence, only membrane is mentioned. Next, in Figure 4A, we confirmed S14 localization on IMC by treating sporozoites with Triton X-100 and colocalizing with IMC proteins GAP45 and MTIP.

134-135 In which species?

Response: We have mentioned P. berghei in the text in the revised manuscript.

141-142 Please include images of blood stage and liver stage parasites.

Response: Blood and liver stage images are included in the revised manuscript as Figure S2.

142-143 Which membrane?

Response: Live S14-mCherry localization on the membrane does not differentiate between the outer membrane or IMC. Hence, only membrane is mentioned. Next, in Figure 4A, we confirmed S14 localization on IMC by treating sporozoites with Triton X-100 and colocalizing with IMC proteins GAP45 and MTIP.

148-149 I cannot find the specific figure you refer to; I checked the online version of the Frenal 2010 paper.

Response: Electromobility shifts of GAP45 due to the palmitoylation have been reported in (Rees-Channer et al, 2006; DOI: 10.1016/j.molbiopara.2006.04.008). Frenal 2010 paper has stated about two bands but experimentally, it was shown in Rees-Channer et al, 2006 in Figures 1 and 2B.

175 gland, we counted [...]

Response: Corrected.

177 Compared to the

Response: Corrected.

177-179 Failed to invade (absolutely)? Or invaded in highly reduced numbers?

Response: Corrected.

182-186 Please be precise: I think you mean you let all types of mosquitoes take a blood meal; s14 knockout-infected mosquitoes did not infect mice.

Response: Corrected.

181-202 Perhaps use paragraphs to indicate the different types of experiments performed here.

Response: Done.

204 Please introduce paragraphs to identify the different experiments in this section

Response: Done.

208 Outer or inner membrane of what? IMC, the plasma membrane?

Response: We treated sporozoites with Triton X-100 to analyze whether S14 is present on the outer membrane (plasma membrane) or IMC.

228 onwards Structural models were obtained from whom? Which species did you use for the docking study? Could you use in one approach 3 berghei proteins, and confirm your docking studies with the falciparum proteins? That would strengthen your model. Should you include a negative control protein in the approach? Response: The structural models were obtained using the trROSETTA server. We used P. berghei for the docking study. In the old annotation and RMGM, the ortholog of P. berghei (PBANKA_0605900) in P.falciparum (PF3D7_1207400) was indicated. However, the updated PlasmodDB does not show PBANKA_0605900 ortholog in P. falciparum. We did try to generate structure models of P. falciparum MTIP, GAP45 and S14 using the trROSETTA server. We successfully reproduced the structure of MTIP, and GAP45 but the quality of S14 structure was unsuitable for the interaction studies. The negative control cannot be included in this kind of study because it gives a false interface, and none of the previous studies have used negative control.

250-251 Was all of the gene cloned? Please define amino acid range. discussion

Response: Full-length gene of S14, MTIP and GAP45 was cloned and the same has been mentioned in materials and methods in the revised manuscript.

Please discuss data from https://elifesciences.org/articles/77447 in relation to your protein Response: Discussed.

298-300 More recent glideosome papers exist. For example https://doi.org/10.1038/s42003-020-01283-8

Response: Included.

340 List the proteins you analysed. Add URL (websites) to the analyses tools.

Response: They are listed in Table S1. The method section gives all the URLs with references, lines 348-358 in the revised manuscript.

343 Known association from the literature: how was this done?

Response: The interactions demonstrated by different groups have been summarized in the review by Boucher & Bosch, 2015 (doi: 10.1016/j.jsb.2015.02.008).

346-349 A few glideosome components? On what basis were they selected and which are they? Response: The analysis showed that S14 had properties similar to GAP45 and MTIP. Additionally, S14 localized with GAP45 and MTIP, hence selected for interaction studies.

471 Can AlphaFold Structure Predictions be used in the docking studies?

Response: Even the Alphafold AI is trained on existing sequence/structure information despite being advertised as a de novo prediction system. That's why it can't produce good quality structures of evolutionarily unique proteins such as S14. We initially started our protein model generation by alphafold2, but the quality of the structure was very low; then we further used the trRosetta server (https://yanglab.nankai.edu.cn/trRosetta/), which shows the quality of all three protein structures above 95 after validation by using UCLA-DOE LAB-SAVES V6.0 (https://saves.mbi.ucla.edu/).

tr-Rosetta includes inter-residue distance, orientation distribution by a deep-neural network, and homologous template to improve the accuracy of models (DOI: 10.1038/s41596-021-00628-9).

We have given the model structure generated using alphafold2 for your reference.

Model generated by using AlphaFold2.ipynb (https://colab.research.google.com/github/sokrypton/ColabFold/blob/main/AlphaFold2.ipynb#scrollTo=kOblAo-xetgx).

Structure quality assessment by __http://saves.mbi.ucla.edu/.__

GAP 45

__S14 __

MTIP

487 What parts of theses genes was cloned? Define the amino acid range.

Response: The full-length protein-encoding gene was cloned.

714 Please split the table into A Mosquito bite and B haemolymph Sporozoites Response: Done.

Figure 1 For clarity, maybe write S14::mCherry

Response: Done.

Figure 1 It would be useful to show blood stage parasite images.

Response: Blood stage parasite image is included in the revised manuscript as Figure S2.

Figure 2G Haemolymph sporozoites ?

Response: Done.

Figure 8 You argued that S14 is a membrane-bound protein through palmitoylation. Here the protein is shown to be cytoplasmic. Please update our model with more recent ones. Response: We have shown that S14 colocalizes with GAP45 and MTIP, suggesting its IMC localization. We have updated our model in Figure 8.

Figure S2B It would be good to include a positive control for these PCRs.

Response: We have replaced the figure's new gel with a positive control.

Figure S3 It would be good to include a positive control for these PCRs. Response: We already have positive controls in Figure S3C and S3F for all the primer pairs used.

Tabel S1 Table S1 is only mentioned twice in the text: lines 124 and 128. There is no mention that the table contains all (??) known gliding motility proteins.

Response: The table does not contain all the gliding proteins; however, most of the proteins mentioned in the Boucher & Bosch, 2015 paper (doi: 10.1016/j.jsb.2015.02.008) were included.

Table S1 The algorithms / websites used for bioinformatic prediction need to be listed here.

Response: Included.

Table S2 Add the plasmodb gene identifiers here. The table does not show all Plasmodium spp. but a selection. Response: All the orthologs mentioned in Figure S1 and Table S2 are not shown in the updated PlasmoDB. Accordingly, we have removed the Figure S1 and Table S2 in the revised manuscript__.__

Reviewer #1 (Significance (Required)):

General assessment: The authors provide an in-depth analyses of the Plasmodium berghei protein S14 and its involvement in gliding motility. Response: Thank you.

Advance: This paper is the first analysis of the S14 protein. The authors suggest a bridging function for the protein between MTIP and GAP45. Response: Thank you.

Audience: Gliding motility is of interest to the apicomplexan field. I think this particular proteins is specific to Plasmodium spp. Response: Thank you.

Reviewer #2

Summary:

The authors tag the sporozoite protein S14 in P. berghei and show localization near the sporozoite plasma membrane. They also convincingly show, through the generation of S14 knockout lines, that S14 is required for sporozoite motility and thereby also salivary gland and hepatocyte invasion. Their bioinformatic results support possible interactions between S14 and the inner membrane complex proteins MTIP and GAP45. These analyses were performed with these specific candidate proteins rather than being unbiased searches for potential interaction partners. The yeast 2-hybrid data to support these possible protein interactions need further controls.

Lines 143-144: Unless the sporozoites were not permeablized prior to staining, it is not clear if the protein is "on" the plasma membrane or just under the plasma membrane. Furthermore, this statement anyway seems contradictory to the authors' interpretation of Figure 4A. Response: Live S14-mCherry localization on the membrane does not differentiate between the outer membrane or IMC. Next, in Figure 4A, we confirmed S14 localization on IMC by treating sporozoites with Triton X-100 and colocalizing with IMC proteins GAP45 and MTIP. Further, we ensured that mCherrey signals were bleached post-fixation and performed IFA with and without permeabilization. We revealed the mCherry and CSP signals using Alexa 488 and Alexa 594, respectively. We observed the mCherrey signal with permeablized sporozoites, not without permeabilization.

Line 218: "This result indicates that S14 is present within the inner membrane of sporozoites." While this data shows that S14 is not in the plasma membrane of the parasite, how can the authors be sure it is at the IMC? Response: S14 colocalization with MTIP and GAP45 suggested its localization on IMC.

Line 225-226: This sentence overreaches in its conclusion. There is no indication that this protein provides the power or force behind the sporozoites forward movement. Several proteins are known to be required for gliding motility, but they are not all force-providing factors. Response: We have modified the sentence, and now it states, ‘These data demonstrate that S14 is an IMC protein, essential for the sporozoite's gliding motility.

Minor comments:

Line 99: "the role of gliding-associated proteins is unexplored" There are several publications on GAP40, GAP45 and GAP50 (some of which are referenced in the previous paragraph). Response: We have included the reference for studied proteins and modified the sentence for clarity.

Line 114: "We narrowed it down to a candidate" Narrowed down how? Or rephrase. Response: We identified the S14 gene from the Kaiser et al., 2004 paper (DOI: 10.1046/j.1365-2958.2003.03909.x) and rephrased the sentence in the revised manuscript.

Lines 120-123 are strangely written, and I don't follow the logic. What "similar properties" do GAP45 and GAP50 have with S14 and are they really indicative of function? Also if palmitoylation and myristylation and nonclassical secretion are present in most eukaryotes, why would they necessarily be evidence of IMC targeting? Response: It was wrongly written, we have modified the sentence for clarity.

Line 148-149. I did not see examples of this electromobility shift of GAP45 in this publication (although I may have overlooked it).

Response: Electromobility shifts of GAP45 due to the palmitoylation have been reported in (Rees-Channer et al, 2006; DOI: 10.1016/j.molbiopara.2006.04.008). Frenal 2010 paper has stated about two bands, but experimentally it was shown in Rees-Channer et al, 2006 in Figure 1 and 2B.

Table 1 legend should preferably specify that hemolymph sporozoites were used for IV infections. Response: Done.

Line 228: Should be rephrased for accuracy. "revealed the" should be replaced with "suggests" Response: Replaced.

Lines 305-307: I don't entirely understand the logic laid out here.

Response: This was written about GAP45 and MTIP coordination; however, it has been removed in the revised manuscript.

Lines 320-322: "We hypothesize that S14 possibly plays a structural role and maintains the stability of IMC required for the activity of motors during gliding and invasion." The data about the IMC structure shown is fluorescence microscopy - and there no change is observed in the IMC in the knockout line. I suggest removing or rephrasing this point if no extra data is provided to show this. Response: We have removed this sentence in the revised manuscript.

Reviewer #2 (Significance (Required)):

The work gives insights into an unstudied, conserved Plasmodium protein, S14, which the authors show is critical for Plasmodium transmission from mosquitoes. The parasite genetics and phenotyping demonstrating this are strong. The conclusions about interactions with glideosome/inner membrane complex components need further experimental support. The work is of interest to the Plasmodium field and may be also of interest to people interested in other protozoan parasites or in cellular motility.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

The manuscript by Gosh and colleagues demonstrates that S14 is a glideosome-associated protein in sporozoites. S14 knockout sporozoites fail to infect mosquito salivary glands and liver cells in the mammalian host. These sporozoites are also defective in gliding motility as S14 localizes to the inner membrane. S14 was shown to interact with the glideosome-associated proteins GAP45 and MTIP using the yeast two-hybrid system. The authors also provide an in-silico prediction on the S14, GAP45 and MTIP interaction.

Major issues:

Overall, there is information lacking in the manuscript, including on the figure legends, regarding experiments replication and n analyzed.

For complementation, the authors engineered an independent S14 knockout line. For this line is clear that parasites failed to infect salivary glands contrarily to the knockout line. Despite not showing it, did the authors confirm that this knockout line has no defects in infecting mosquito midguts and producing sporozoites? Response: We analyzed the midgut for sporozoite formation, which was comparable to the original KO line, and included the data (Figure 2D) in the revised manuscript.

Did the authors conduct IV injections in mice with a higher number of sporozoites? Hemolymph sporozoites are less infectious than sporozoites collected from the salivary glands and I was wondering whether patent infections with S14 ko sporozoites can be obtained by injecting a higher inoculum. The same applies to the infectivity experiments with HepG2cells. Response: We increased the sporozoites dose and infected mice with 10,000 hemolymph sporozoites, but no infection was observed (Table 1). No EEFs were observed in HepG2 cells infected with 10,000 S14 KO hemolymph sporozoites.

Please provide information on the number of sporozoites that were analyzed in the trails experiment. Response: We analyzed 210, 225, and 212 sporozoites for WT GFP, S14 KO c1, and S14 KO c2, respectively.

Minor issues:

In Figure 1. F) WB on S14-3xHA-mCherry tagged sporozoites showing two bands on the WB. The Palm-band is only inferred thus I suggest correcting the figure to S14-3xHA-mcherry. On 1D all the mcherry signal is detected on the membrane but then on WB, a smaller fraction is palm? What is the explanation for the ratio between the two bands? Why so distinct CSP intensity bands between wt and tagged line? Were very distinct amounts of protein loaded?

Response: We have corrected the Palm-S14-3xHA-mcherry to S14-3xHA-mcherry.

This reviewer raises a valid point regarding the discrepancy between IFA and Western blot. The non-palmitoylated S14-mCherrey signal was possibly corrected after deconvolution in image 1D and mainly the membrane signal was prominent. In Figure 1C, many sporozoites show some cytosolic signal, perhaps representing non-palmitoylated S14. Western blot concentrates the protein of interest as a single band, allowing more accurate visualization of protein.

The distinct CSP intensity bands between wt and the tagged line are due to the loading of a higher amount of parasite lysate in WT lane. To ensure that the western blot signal is specific to S14, we loaded a higher amount of protein in WT.

Figure 1. A) Statistical analysis is missing. Not clear if the bars represent mean values +/- standard deviation. No information on the material and methods of how the relative expression was calculated. Response: No error bars are shown in Figure 1 because it was performed once.

In the introduction lines 54 and 58 I suggest replacing humans with mammalian host. Response: Replaced.

Line 58. Not clear why the ref Ripp et al., 2021 is used for a general sentence to introduce the Plasmodium life cycle. Response: Removed.

Line 72: I suggest replacing "TRAP mutant" with "TRAP knockouts" (Sultan et al., 1997). More recently there are TRAP mutants with impaired motility and normal invasion of mosquito salivary glands (Klug et al., 2020) Response: Replaced.

Lines 78 to 86: In this paragraph, authors refer to several proteins involved in sporozoite gliding motility and host cell invasion, however for most of the studies this conclusion comes from the characterization of knockouts defective phenotype and actually a direct role for some of these molecules in the process awaits clear demonstration. Response: We have replaced involved with implicated.

Line 78: Authors do not consider that maebl knockout sporozoites display reduced adhesion, including to cultured hepatocytes, which could contribute to the defects in multiple biological processes, such as in gliding motility, hepatocyte wounding, and invasion. Response: We have corrected maebl role in the revised manuscript.

Line 80: I suggest authors reconcile the contradictory reports in the literature on the role of TRSP in sporozoites invasion. Response: We have removed this reference in the revised manuscript.

Line 82-83: Please revise it. Response: Revised.

Table 1. Correct table as when sporozoites were transmitted by mosquito bite the term "number of sporozoites injected" does not apply. Please give more details on the bite experiments. Is this the number of mosquitoes for all four animals? For how long the mosquitoes were allowed to bite? Response: For clarity, we have split the table into A Mosquito bite and B haemolymph Sporozoites. We used ten mosquitoes/mice in the bite experiment. Mosquitos were allowed to probe for blood meal for 20 minutes, and the feeding was ensured by observing mosquitoes post-blood meal; approximately 70% of mosquitoes received the blood meal in all the cages.

Line 288 and 289. There are several publications showing that maebl knockout sporozoites are impaired at invading the mosquito salivary glands and at infecting the vertebrate host contradicting Kariu et al., 2002 findings in the vertebrate host. Response: We have removed maebl from this line.

Line 290. I suggest "was most likely due to" instead of " due to" as sporozoite adhesion to cells was not evaluated. Response: Corrected.

Line 291: "Cellular transmigration and host cell invasion are prerequisites for gliding motility" please revise. Response: Revised.

Line 437: indicate which clone was used.

Response: Indicated (3D11).

Line: 463: indicate the % of the gel in the SDS-PAGE Response: We have used 10% SDS-PAGE gel and it is indicated in the revised manuscript.

Line 499: indicate the version of the GraphPad Prism software. Response: GraphPad Prism version 9.

Figure S3 legend needs to be corrected. Panels in the figure are from A to F while in legend G and H are included. Response: Corrected.

4. Description of analyses that authors prefer not to carry out

Reviewer #2

Line 39-41: "Using in silico and the yeast two-hybrid system, we showed the interaction of S14 with the glideosome-associated proteins GAP45 and MTIP. Together, our data show that S14 is a glideosome-associated protein" Although these interactions can be speculated based on the results shown, these interactions were not confirmed in this study. Response: We attempted to pulldown the S14 interacting partner using anti-mCherry antibody from S14-3XHA-mCherry transgenic sporozoites and then further tried to identify interactome using mass spectrometry but failed. Hence, we selected two known IMC localized gliding proteins MTIP and GAP45. Performing pull-down from sporozoites is challenging, so we checked this interaction using yeast 2-hybrid assay and bioinformatic analysis for protein-protein interaction.

In order to claim interaction between S14 and IMC proteins, interaction needs to be shown experimentally. Well-controlled yeast 2-hybrid would be a start - then interaction would be more than just speculative. But immunoprecipitation from sporozoites or other biochemical interactions would give more support to this idea. Response: We attempted to pulldown the S14 interacting partner using an anti-mCherry antibody from S14-3XHA-mCherry transgenic sporozoites and then further tried to identify interactome using mass spectrometry but failed. Hence, we selected two known IMC localized gliding proteins MTIP and GAP45. Performing pull-down from sporozoites is challenging, so we checked this interaction using yeast 2-hybrid assay and bioinformatic analysis for protein-protein interaction.

Reviewer #3

The authors provide convincing data on the S14 localization in the inner membrane of sporozoites and interaction with GAP45 and MTIP using the yeast model. Did the authors consider conducting co-IP followed by MS analysis to pull down S14 in the complex with GAP45 and MTIP? Response: We attempted to pulldown the S14 interacting partner using an anti-mCherry antibody from S14-3XHA-mCherry transgenic sporozoites and then further tried to identify the interactome using mass spectrometry but failed. Hence, we selected two known IMC localized gliding proteins, MTIP and GAP45. Performing pull-down from sporozoites is challenging, so we checked this interaction using yeast 2-hybrid assay and bioinformatic analysis for protein-protein interaction.

__Reviewer #3 (Significance (Required)):____ __ Sporozoite gliding motility is a critical feature of parasite infectivity. Impairment of this important feature has been described for several mutant/knockout parasite lines. This study goes beyond the phenotypic analysis of mutant parasites to infer the role of S14 by providing more mechanistic evidence to show S14 interaction with other glideosome-associated proteins. However, this interaction was investigated using the two-hybrid system in yeast. Still, in sporozoites, no experiments were conducted to evaluate the interaction between these proteins.

Response: We attempted to pulldown the S14 interacting partner using an anti-mCherry antibody from S14-3XHA-mCherry transgenic sporozoites and then further tried to identify interactome using mass spectrometry but failed. Hence, we selected two known IMC localized gliding proteins, MTIP and GAP45. Performing pull-down from sporozoites is challenging, so we checked this interaction using yeast 2-hybrid assay and bioinformatic analysis for protein-protein interaction.

Please consider I'm not an expert on the in-silico interaction studies.

Matthew Stone History of Electronic Media MHP Peer Review 11/12/23 The first thing I would like to point out in this peer review is the beginning of your paper. The introduction explaining educating the masses, and how edutainment came to be was a very interesting way to start the paper and definitely works well with your topic of nature documentaries. I thought that the opening paragraph at whole was a great introduction into what exactly nature documentaries are and definitely brings some questions up for the reader to contemplate, such as why are humans drawn to nature documentaries? What about nature documentaries makes them such great forms of both entertainment and educational content? Among other questions the reader may be asking themselves. I really like that right away in the second paragraph you begin answering questions the reader may have with facts backed up by sources, like when you brought up the experiment in which half of the students watched a nature documentary on marine mammals and the other half was given a verbal lesson on marine mammals, and explained how the half that watched the documentary had better attitudes on the subject matter at hand. This example alone gives the reader a better understanding of how impactful nature documentaries can be. One thing that could be improved here in my opinion is doing a bit more to explain how motion pictures create a deeper bond between viewers and the subject matter. While I do like your explanation at the end of the second paragraph, I just personally feel that maybe another sentence or two going more in depth on this explanation may be a good addition. I really have no complaints about the third paragraph, as I feel you do a pretty good job depicting the founding fathers of the nature documentary and crediting each of them for what they did quite well. For the fourth paragraph, I feel you could’ve gone more in depth into the merging of narration alongside film of animals that created the nature documentaries we know today.<br /> Lastly I think what this paper is lacking most is a nice conclusion paragraph to kind of put the reader at ease with what they just read. As it is right now this is a pretty good paper but without any overall statements or ending paragraph, the ending of this paper leaves the reader feeling a bit left off without an overall statement from the paper. I just personally think the paper needs one to two more paragraphs (potentially an extra body paragraph, but for sure an ending paragraph) to neatly wrap the paper up in an informative and entertaining way, kind of like edutainment! However, overall, I liked this paper a lot and as a fan of nature documentaries I love that you picked that as your topic for this paper!

This work has been peer reviewed in GigaScience (see https://doi.org/10.1093/gigascience/giad092), which carries out open, named peer-review. This review is published under a CC-BY 4.0 license:

**Reviewer Name: Zhenbin Hu **

In this MS, the authors tried to develop a framework for using GBS data for downstream analysis and reduce the impact of sequence errors caused by GBS. However, sequence error is an issue not specific to GBS, it is also for whole genome sequences. Actually, I think the major issue for GBS is the missing data. However, in this MS, the authors did not test the impact of missing data on downstream analysis.The authors also mentioned that sequencing error may cause distortion segregation in linkage map construction, however, distortion segregation in linkage map construction can also happen for correct genotyping data. The distortion segregation can be caused by individual selection during the construction of the population. So I don't think it is correct to use distortion segregation to correct sequence errors.The authors need to clear the major question of this MS, in the abstract, the authors highlight the sequence errors, while in the introduction, the authors highlight the package for linkage map construction (the last paragraph). Actually, from the MS, authors were assembling a framework for genotyping-by-sequencing data.Two major reduced-represented sequencing approaches, GBS and RADseq, have specific tools for genotype calling, such as Tassel and Stack. However, the authors used the GATK and Freebayes pipeline for variant calling, authors need to present the reason they were not using TASSEL and Stack.In the genotyping-by-sequencing data, individuals were barcoded and mixed during sequencing, what package/code was used to split the individuals (demultiplex) from the fastq for GATK and Freebayes pipeline?The maximum missing data was allowed at 25% for markers data, how about for the individual missing rate?On page 6, the authors mentioned 'seuqnece size of 350', what that means?

This work has been peer reviewed in GigaScience (see https://doi.org/10.1093/gigascience/giad085 ), which carries out open, named peer-review. The review is published under a CC-BY 4.0 license:

Reviewer name: Raphael Leman

Summary: In this work Barbosa et al., presented a benchmarking of several splicing predictors for human intronic variants. Overall, the results of this study shown that deep learning based tools such as SpliceAI outperformed the other splicing predictors to detect splicing disturbing variants and so pathogenic variants.

The authors also detailed the performances of these tools on several subsets of data according to the collection origins of variants and according to the genomic localization of variants. This work is one of the first large and independent studies about splicing prediction performances among intronic variants and in particular among deep intronic variants in a context of molecular diagnosis. This work also highlights the need to have reliable prediction tools for these variants and that the splicing impact of these variants are often underestimated. However, I estimated that major points should to be solved before considering the article to publication.

**Major points ** 1 The most important point is that authors shown results in the main text but in following paragraphs they claimed that these results were biased. In addition, the results, taking into account these biases, were only shown in supplementary data and the readers should make the correction themselves to get the "true" results. Indeed, the interpretation of biased results and "true" results changes drastically. The two main biases were: i) the use of ClinVar data already used for the training of CAPICE (see my following comment n°2-), ii) the intronic tags of variants and the relative distance to the nearest splice site were wrong (see my following comment n°5-). Consequently, the authors should remove these biased results and only show results after bias correction.

2 Importantly, several tools used ClinVar variants or published data to train and/or validate their models. Therefore, to perform a benchmark on true independent collection of variants, the authors should ensure the lack of overlapping between variants used for the tool development and this present study.

3 As authors shown by the comparison between the ClinVar classification (N = 54,117 variants) and impact on RNA from in vitro studies (N = 162 variants), there was discrepancies between this two information (N = 13/74 common variants, 18%). Consequently, using ClinVar classification to assay the performance of splicing prediction tools is not optimal. To partially fix this point, I think further studying (ex: get minor allele frequency, availability of in vitro RNA studies, …) the intronic variants with positive splicing predictions from two or more tools with a ClinVar classification benign or likely benign and inversely, the intronic variants with negative splicing predictions from two or more tools with a ClinVar classification pathogenic or likely pathogenic could be interesting.

4 The authors used pre-computed databases for 19 tools, but the most of these databases do not include small insdels and so add artificially missing data in disfavor of the tool although the same tool could score these indels variants in de novo way.

5 The authors said that "We hypothesized that variability in transcript structures could be the reason [increase in performance in the deepest intronic bins]: despite these variants being assigned as occurring very deep within introns (> 500bp from the splice site of the canonical isoform) in the reference isoform, they may be exonic or near-splice site variants of other isoforms of the associated gene". To solve this transcript structure variability, firstly the authors could use weighted relative distance as following: |(|Pos_(nearest splice site)-Pos_variant |)-Intron_Size |â•„(Intron_Size ). Secondly, the ClinVar data contains the RefSeq transcript ID on which the variant was annotated (except for large duplications/deletions), so the authors should make the correspondence between these RefSeq transcript IDs and the transcripts used to perform splicing predictions.

6 With respect to the six categories of splice-altering variants, it is unclear how the authors considered cases in which variants alter physiological splice motives (e.g., natural consensus sequences 3'SS/5'SS, branch point, or ESR) but, instead of exon skipping, the spliceosome recruits another distant splice site that is partially or not affected by the variant.

7 In the table 1 listing the tools considered for this study, please explicit for each tool on which collections of data (ClinVar or splicing altering variants) and for which genomic regions the benchmark was done. This information will facilitate the reading of the article.

8 Accordingly to my comment n°3-, all spliceogenic variants are not necessary pathogenic. The mutant allele could produce aberrant transcripts without a frame-shift and without impact the functional domains of the protein. In addition, the transcription could also lead to a mix between aberrant transcript and full-length transcript. As a result, the main goal of splicing prediction tools is to detect splicing altering varaints. Considering variants with positive splicing prediction as pathogenic is a dangerous shortcut and only an in vitro RNA study could confirm the pathogenicity of a variant. The discussion section should be update in this sense.

9 The authors claimed that: "The models [SQUIRLS and SPiP] were frequently able to correctly identify the type of splicing alteration, yet they still fail to propose higher-order mechanistic hypotheses for such predictions.". I think that the authors over-interpreted the results (see my comment n° 21-).

10 The authors recommended prioritizing intronic variants using CAPICE, It is still true once the bias was corrected (see my comment n°1-).

**Minor points **

11 In the introduction the authors could clearly define the canonical splice site regions (AG/GT dinucleotides in 3'SS: -1/-2 and 5'SS: +1/+2) to make the difference with the consensus splice sites commonly define as: 3'SS: -12 (or -18)/+2 and 5'SS: -3/+6. 12 In the introduction, please also add that splice site activation could be also due to disruption of silencer motif. 13 In the ref [17], the authors did not say that the enrichment of splicing related variants within splice site regions was linked to exons and splice sites sequencing. They proved that whole genome sequencing increased the diagnostic rate of rare genetic disease, actually they did not focus on splicing variants. This enrichment was more probably induced by the fact that geneticists mainly studied variants with positive splicing predictions. 14 In the paragraph 'The prediction tools studied are diverse in methodology and objectives', please add that most of prediction tools target consensus splice sites (ex: MES, SSF, SPiCE, HSF, Adaboost, …).

15 In the paragraph 'The prediction tools studied are diverse in methodology and objectives', the authors claimed that 'sequence-based deep learning models such as SpliceAI, which do not accept genetic variants as input.' but it is wrong as SpliceAI could accept VCF file as input. 16 In the paragraph 'Pathogenic splicing-affecting variants are captured well by deep learning based methods', this is further explained in the section method, but I think a sentence explaining that the 243 variants were from 81 variants described in ref [19] and 162 variants from a new collection will clarify the reading of article 17 In the paragraph 'Pathogenic splicing-affecting variants are captured well by deep learning based methods', among the 13 variants incorrectly classified, please detailed how many variants were classified as benign and VUS. 18 Due to the blue gradient, the Fig 1C is hard to analyze. 19 In the paragraph 'Branchpoint-associated variants', the variant rapported in the ref [79] were studied within tumoral context and so the observed impact could not be the same in healthy tissue. 20 In the paragraph 'Exonic-like variants', the authors changed the parameters of SpliceAI predictions, from the original prarameters used for the precomputed scores, to take into account variants located deep inside the pseudoexon. Please ensure whether other prediction tools have also user-defined optimizable parameters to take into account these variants. 21 In the paragraph 'Assessing interpretability', the authors observed that non-informative SPiP annotations presented a high score level. This could be explained by the fact of the tool report a positive prediction without annotation only because the model score was high without a relation to a particular splicing mechanism. 22 In the paragraph 'Assessing interpretability', the authors could compare the SpliceAI annotations regarding the abolition/creation of splice sites and their relative positions to the variants to the observed effect on RNA. 23 In the paragraph 'Predicting splicing changes across tissues', by my count the analysis of AbSpliceDNA predictions was done on 89 variants (154 - 65 = 89), if true please indicate clearly in the text. 24 In the method section, paragraph "ClinVar", the 13 variants with discordance between the classification and the observed splicing impact, how many did they have confidence stars. 25 In the method section, paragraph "Disease-causing intronic variants affecting RNA splicing", the authors filtered out variants within the 10 pb around the nearest splice site, please explicit why. 26 In the method section, paragraph "Disease-causing intronic variants affecting RNA splicing", the authors used gnomAD variants as control set, however their threshold of variant frequency is too low (1%). Indeed, some pathogenic variants involved in recessive genetic disorders have a high frequency in population. A threshold of 5% is more appropriate. 27 In the method section, paragraph "Variants that affect RNA splicing", the authors should describe how they considered variants leading to multiple aberrant transcripts and variants with partial effect (i.e., allele mutant still producing full length transcript). 28 In the method section, paragraph "Variants that affect RNA splicing", regarding the six categories defined by the authors: How the indels variants were annotated if they overlapped between several categories.

The new splice donor/acceptor categories included only variants creating new AG/GT or variants occurring within the consensus sequences of cryptic splice sites. Among the category Donor-downstream, please make the distinction between variants located between [+3; +6] bp (i.e. consensus sequence) and variant beyond +6 bp. The exonic-like variants could be variants that did not impact ESRs motives (see my comment n°6-). 29 In the method section, paragraph "Variants that affect RNA splicing", the authors select for the control datasets, variants generating the CAGGT and GGTAAG motives. However, this approach lead to an over-enrichment of false positives. Moreover, it could be also interesting if among the variants creating new splice sites or pseudoexons to identify the presence of GC donor motif or U12-minor spliceosome motif (AT/AC) and how the different splicing tools can detect them. 30 In Fig S3C, scale the gnomAD population frequency in -logₕ₀(P) to make the figure more readable. 31 I saw several times double spaces in the text please correct them. English is not my native language so I am not the best judge, but some sentences seem syntactically incorrect (ex: "The splicing tools with the smallest and largest performance drop between the splice site bin ("1-2") and the "11-40" bin were Pangolin and TraP, with weighted F1 scores decreasing by 0.334 and 0.793, respectively"). Please have the article proofread by someone who is fluent in English.

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** Reviewer name: Urs Greber **

Hirofumi Aso and colleagues provide a manuscript entitled 'Single-cell transcriptome analysis illuminating the characteristics of species specific innate immune responses against viral infections'. The aim was to describe differences in innate immune responses of peripheral blood mononuclear cells (PBMCs) from different primates and bats against various pathogenic stimuli (different viruses and LPS). A major conclusion from the study is that differences in the immune response between primate and bat PBMCs are more pronounced than those between DNA, RNA viruses or LPS, or between the cell types. The topic is of interest as the immunological basis for how bats appear to be largely disease resistant to some viruses that cause severe infections in humans is not well understood. One notion by others has been that bats have a larger spectrum of interferon (IFN) type I related genes, some of which are expressed constitutively even in unstimulated tissue, and there, trigger the expression of IFN stimulated genes (ISGs). Alongside, enhanced ISG levels may need to be compensated for in bats. Accordingly, bats may exhibit reduced diversity of DNA sensing pathways, as well as absence of a range of proinflammatory cytokines triggered in humans upon encountering acute disease causing viruses. The study here uses single-cell RNA sequencing (scRNA-seq) analysis, and transcript clustering algorithms to explore the profile of different innate immune responses upon viral infections of PBMCs from H sapiens, Chimpanzee, Rhesus macaque, and Egyptian fruit bat. Most commonly referred to cell types were detected in all four species, although naïve CD8+ T cells were not detected in bat PBMCs, which led the authors to focus on B cells, naïve T cells, killer T/NK cells, monocytes, cDCs, and pDCs. The study used three pathogenic stimuli, Herpex simplex virus 1 (HSV1), Sendai virus (SeV), and lipopolysaccharide (LPS). Specific comments The text is well written, concise, and per se interesting, but I have a few questions for clarification.

1) Can the authors provide quality and purity control data for the virus inocula to document virus homogeneity? E.g., neither the methods, nor the indicated ref 26 specify if or how HSV1 was purified. Same is true for SeV where the provided ref 34 does not indicate if virus was purified or not. If virus inocula were not purified then it remains unclear to what extent the effects on the PBMCs described in the study here were due to virus or some other component in the inoculum. Conditions using inactivated inoculum might help to clarify this issue.

2) What was the infection period? Was it the same for all viruses?

3) Upon stimuli application, there was a noteable expansion of B cells and a compression of killer T / NK cells in the bat but not the human samples, as well as compression of monocytes, the latter observed in all four species. Can the authors comment on this observation?

4) Lines 78-79: I do not think that TLR9 ought to be classified as a cytosolic DNA sensor. Please clarify.

5) Line 117: please clarify that the upregulation of proinflammatory cytokines, ISGs and IFNB1 was measured at the level of transcripts not protein.

6) Line 244: DNA sensors. Authors report that bats responded well to DNA viruses, although some of their DNA sensing pathways (e.g., STING downstream of cGAS, AIM2 or IFI16) were attenuated compared to primates (H sapies, Chimpanzee, Macaque). And they elute to the dsRNA PRR TLR3. But I am not sure if TLR3 is the only PRR to compensate for attenuated DNA sensing pathways. The authors might want to explicitly discuss if other RNA sensors, such as RIG-I-like receptors (RIG-I, LGP2, MDA5) were upregulated similarly in bats as in primate cells upon inoculation with HSV1.

7) Is it known how much TLR3 protein is expressed in bat PBMCs under resting and stimulated conditions? Same question for the DNA and RNA sensor proteins, e.g., cGAS, AIM2 or IFI16, RIG-I, LGP2, MDA5, or effector proteins, such as STING.

8) Can authors clarify if cGAS is part of the attenuated DNA sensors in the bat samples under study here? And it would be nice to see the attenuated response of DNA sensing pathways in the bat samples, as suspected from the literature, including STING downstream of cGAS, or AIM2 and IFI16.

9) What are the expression levels of IFN-I and related genes in the bat cells among the different stimuli?

10) Technical point: where can the raw scRNA-seq data be found?

Reviewer #2 (Public Review):

Summary:

We often have prior expectations about how the sensory world will change, but it remains an open question as to how these expectations are integrated into perceptual decisions. In particular, scientists have debated whether prior knowledge principally changes the decisions we make about the perceptual world, or directly alters our perceptual encoding of incoming sensory evidence.

The authors aimed to shed light on this conundrum by using a novel psychophysical task while measuring EEG signals that have previously been linked to either the sensory encoding or response selection phase of perceptual choice. The results convincingly demonstrate that both features of perceptual decision-making are modulated by prior expectations - but that these biases in neural process emerge over different time courses (i.e., decisional signals are shaped early in learning, but biases in sensory processing are slower to emerge).

Another interesting observation unearthed in the study - though not strictly linked to this perceptual/decisional puzzle - is that neural signatures of focused attention are exaggerated on trials where participants are given neutral (i.e. uninformative) cues. This is consistent with the idea that observers are more attentive to incoming sensory evidence when they cannot rely on their expectations.

In general, I think the study makes a strong contribution to the literature and does an excellent job of separating 'perceiving' from 'responding'. More perhaps could have been done though to separate 'perceiving' and 'responding' from 'deciding' (see below).

Strengths:

The work is executed expertly and focuses cleverly on two features of the EEG signals that can be closely connected to specific loci of the perceptual decision-making process - the SSVEP which connects closely to sensory (visual) encoding, and Mu-Beta lateralisation which connects closely to movement preparation. This is a very appropriate design choice given the authors' research question.

Another advantage of the design is the use of an unusually long training regime (i.e., for humans) - which makes it possible to probe the emergence of different expectation biases in the brain over different timecourses, and in a way that may be more comparable to work with nonhuman animals (who are routinely trained for much longer than humans).

Weaknesses:

In my view, the principal shortcoming of this study is that the experimental task confounds expectations about stimulus identity with expectations about to-be-performed responses. That is, cues in the task don't just tell participants what they will (probably) see, but what they (probably) should do.

In many respects, this feature of the paradigm might seem inevitable, as if specific stimuli are not connected to specific responses, it is not possible to observe motor preparation of this kind (e.g., de Lange, Rahnev, Donner & Lau, 2013 - JoN).

However, the theoretical models that the authors focus on (e.g., drift-diffusion models) are models of decision (i.e., commitment to a proposition about the world) as much as they are models of choice (i.e., commitment to action). Expectation researchers interested in these models are often interested in asking whether predictions influence perceptual processing, perceptual decision, and/or response selection stages (e.g., Feuerriegel, Blom & Hoogendorn, 2021 - Cortex), and other researchers have shown that parameters like drift bias and start point bias can be shifted in paradigms where observers cannot possibly prepare a response (e.g., Thomas, Yon, de Lange & Press, 2020 - Psych Sci).

The present paradigm used by Walsh et al makes it possible to disentangle sensory processing from later decisional processes, but it blurs together the processes of deciding about the stimulus and choosing/initiating the response. This ultimately limits the insights we can draw from this study - as it remains unclear whether rapid changes in motor preparation we see reflect rapid acquisition of new decision criterion or simple cue-action learning. I think this would be important for comprehensively testing the models the authors target - and a good avenue for future work.

Author Response

Reviewer #1 (Public Review):

This paper examines different signaling networks and attempts to give general results for when the network will exhibit biphasic behavior, which is the situation when the output of the network is a non-monotonic function of its inputs. The strength of the paper is in the approach it takes. It starts with the simplest network motifs that produce biphasic behavior and then asks too what happens when these motifs are parts of larger networks. Their approach is in contrast to the usual way in which this question is tackled, which tends to be within the confines of a specific signaling network, where general results like the ones that the authors are after, might be hard to spot.

We thank the reviewer for the careful reading of the manuscript and for the comments and appreciate the fact the reviewer regards the approach as the strength of the paper.

The weakness of the paper, in my opinion, is the rather formal description of the results which I am afraid will be of rather limited utility to experimental groups seeking to make use of them. The paper attempts to provide general rules for when to expect biphasic behavior and it was hard to assess to what extent such rules exist as behaviors can change depending on the context of a larger network in which the smaller biphasic one is embedded. The other thing that made assessing the generality of the results difficult is that the input-output functions shown in all the figures are computed for a specific choice of parameters and I was left wondering how different choices of parameters might change the reported behaviors. The lack of specific proposals for how their results should guide future experiments on different signaling networks is another weakness.

We address these points in a number of ways. Initially our presentation was intended to highlight unambiguously which systems (especially the substrate modification building blocks) were capable of biphasic response and which were not, and highlighting parameter dependence on intrinsic kinetic parameters. Based on both referee comments, we make a number of changes

(a) We highlight the rationale for choosing the suite of biochemical substrate modification systems: enzyme/substrate sharing is a key driver for the origins of biphasic responses and the suite of systems we employ allows us to systematically explore this (see Response to Essential Revisions). These are building blocks of many pathways,

(b) Biphasic responses emerge from a built in competing effect. In every instance of substrate modification systems, we now highlight the mechanistic underpinning which gives rise to the competing effect responsible for the biphasic response. This will help experimentalists and modellers alike obtain insights into how such behaviour may arise, and the associated ingredients which facilitate that (which may be relevant in other systems). Similarly, we highlight how altered behaviour at the network level may arise from a biphasic interaction pattern, providing the intuition therein and guide further experimental investigation (also see Response to Essential Revisions).

(c) With regard to parameters (also see Response to Essential Comments) firstly we emphasize that we completely characterize at the substrate modification level, whether biphasic responses are possible as a function of intrinsic kinetic constants. This is done for every system studied. In Fig 2, we depict this, along with sample biphasic dose responses, for pictorial depiction. However, the essential point is that the parametric dependence on intrinsic kinetic parameters is completely done. We indicate in which cases biphasic responses are impossible irrespective of intrinsic kinetic parameters, where they can be obtained for every value of the intrinsic kinetic parameters, and where there are partial restrictions in the intrinsic kinetic parameter space for obtaining this. In the revision we have performed further parametric analysis to assess the impact of species total amount providing further insights. We have also shown that in all these systems biphasic responses can be obtained in ranges of kinetic parameters similar to those found experimentally (eg Wistel et al 2018) and for reasonable species total amounts in systems and synthetic biology. This is analyzed, and depicted in Figure 2-figure supplement 3 and Figure 2-figure supplement 4.

(d) Also, in response to another comment (about behaviour changing in networks): we first emphasize that we start at the substrate modification level to uncover drivers of biphasic responses at this level. Biphasic responses arise from an inbuilt competing effect and we demonstrate different ways in which such an inbuilt competing effect arises, through sharing of enzymes or substrates. While it is true that the behaviour can change as part of a network (a) It still remains that there are these in-built competing effects which can generate biphasic responses (both substrate and enzyme) and this can manifest at a pathway or network level under suitable conditions (b) the fact that behaviour at a network level may be altered is exactly why we consider studies at the network level showing both biphasic patterns in interaction (the overall behaviour is determined by the motif and the biphasic pattern of interaction and studies involving interaction of biphasic responses at both the network and substrate modification level!! (subsection: The network level)

(e) We have also expanded on a paragraph on testable predictions in the conclusions (p10).

Taken together, we believe that these results should interest both experimentalists and modellers and have intrinsic value as well.

While I appreciate that the authors adopted a style of presenting their results such that all the mathematics is buried in the figures, I found that it made reading the paper quite difficult, and contributed to my confusion about which results are general and insensitive to parameter choices and which are not. I believe a narrative that integrated the math with some simple intuition might have been more effective. For example, when the authors say in the text that model M0 is incapable of displaying biphasic response, how general is that result? Later on, when discussing model M2, they provide a criterion for biphasic response in terms of products of rate constants satisfying an inequality, but the meaning of this condition is not described. Such things make it hard to learn from the authors' work.

This has indeed been incorporated, and we agree that presenting the intuition and mechanistic underpinning for the behaviour aids readability. In addition to the points about parameters which are now explained at length in the paper , there are a number of paragraphs providing the mechanistic underpinning and intuition for why the behaviour is obtained. Both these are discussed at length in Response to Essential Revisions. Thus, both the mechanistic intuition and the role of parameters are addressed in detail in the revision.

When M0 is mentioned to be incapable of yielding biphasic responses we mean just that: irrespective of any parameter choice in the model. The meaning of the criterion in Model M2 is now discussed. We take the point about not being able to learn from the work seriously and have made various changes both on the intuition and clarifying the impact of parameters.

The text is sprinkled with statements like "this reveals the plurality of information processing behaviors..." where the meaning is quite opaque (for this example, there is no description of "information processing" and what it might mean in this context) and therefore it makes it hard to understand what are the lessons learned from these calculations. Another example is found in the description of Erk regulation where the authors speak of "significant robustness" but what is meant by "significant" is also unclear.

Yes, we agree that these phrases are distracting and not adding much and so we have removed them.

Overall, I think this is an interesting attempt to provide a general mathematical framework for analyzing biphasic response of signaling networks, but the authors fall short for the reasons described above. I think a lot can be fixed by improving the way the results are presented.

We have indeed taken these comments on board and aimed to improve the presentation

Reviewer #2 (Public Review):

Biphasic responses are widely observed in biological systems and the determination of general design principles underlying biphasic responses is an important problem. The authors attempt to study this problem using a range of biochemical signaling models ranging from simple enzymatic modification and de-modification of a single substrate to systems with multiple enzymes and substrates. The authors used analytical and computational calculations to determine conditions such as network topology, range of concentrations, and rate parameters that could give rise to biphasic responses. I think the approach and the result of their investigation are interesting and can be potentially useful. However, the conditions for biphasic responses are described in terms of parameter ranges or relationships in particular biochemical models, and these parameters have not been connected to the values of concentrations or rates in real biological systems. This makes it difficult to evaluate how these findings would be applicable in nature or in experiments. It might also help if some general mechanisms in terms of competition/cooperation of time scales/processes are gleaned which potentially can be used to analyze biphasic responses in real biological systems.

We thank the reviewer for a careful reading of the manuscript and for the various comments and are happy to see the reviewer find the approach interesting. We address these comments in more detail below.

Reading these comments, we recognized how various analysis and algebraic equations could appear opaque to a reader both in terms of what it conveys and its import. To address this, we made a number of changes.

1. First and foremost, we provide the mechanistic underpinning and intuition for why a competing effect emerges in the first place. We do this for every substrate modification system we analyze and make further comments in the subsection focussing on the network level as well as ERK This intuition should help a reader where the result is coming from and be then able to see if it might apply in a quite different system. This is discussed in detail in Response to Essential Revisions.

2. Secondly, we have discussed many aspects of the parameters in more detail. Our goal, especially in substrate modification systems was to be able to completely characterize the role of intrinsic kinetic parameters: whether biphasic responses was impossible irrespective of parameters, whether they were possible for every value of intrinsic kinetic parameters or whether they were possible in a subset of kinetic parameter space. This has been done for every substrate modification system, and has been discussed more explicitly in the revision. Furthermore, when biphasic responses were possible, we aimed to determine the impact of species total amounts which facilitated the response. Here we performed additional analytical and semi-analytical work. Additionally with the semi-analytical work and parameters chosen in ranges very similar to those found experimentally (eg Wistel et al 2018), we are able to show that biphasic responses can indeed be obtained in experimentally feasible ranges. Further aspects of the parameters are discussed in detail in the Response to Essential Revisions. In particular, a number of new paragraphs (p2-3, p6) and plots Figure 2-figure supplement 3 and Figure 2-figure supplement 4 specifically deal with this.

Taken together these address the reviewers points.

Author Response

Reviewer #1 (Public Review):

Due complicated and often unpredictable idiosyncratic differences, comparing fMRI topography between subjects typically would require extra expensive scan time and extra laborious analyzing steps to examine with specific functional localizer scan runs that contrast fMRI responses of every subject to different stimulus categories. To overcome this challenge, hyperaligning tools have recently been developed (e.g., Guntupalli et al., 2016; Haxby et al., 2011) based on aligning in a high-dimensional space of voxels of subjects' fMRI responses to watching a given movie. In the present study, Jiahui and colleagues propose a significantly improved version of hyperaligning functional brain topography between individuals. This new version, based on fMRI connectivity, works robustly on datasets when subjects watched different movies and were scanned with different parameters/scanners at different MRI centers.

Robustness is the major strength of this study. Despite the fact that datasets from different subjects watching different movies at different MRI centers with different scan parameters were used, the results of functional brain topography from between-subject hyperalignment based on fMRI connectivity were comparable to the golden standard of within-subject functional localizations, and significantly better than regular surface anatomical alignments. These results also support the claim that the present approach is a useful improvement from previous hyperalignments based on time-locked fMRI voxel responses, which would require normative samples of subjects watching a same movie.

We thank the reviewer for the appreciation of our work.

Given the robustness, this new version of hyperalignment would provide much stronger statistical power for group-level comparisons with less costs of time and efforts to collect and analyze data from large sample size according to the current stringent standard, likely being useful to the whole research community of functional neuroimaging. That said, more discussions of the limit of the present hyperalignment approach would be helpful to potential eLife readers. For example, to what extend the present hyperalignment approach would be applicable to individuals with atypical functional brain topography such as brain lesion patients with e.g., acquired prosopagnosia? Even in typical populations, while bilateral fusiform face areas can be identified in the majority through functional localizer scans, the left fusiform face area sometimes cannot be found. Moreover, many top-down factors are known to modulate functional brain topography. Due to these factors, brain responses and functional connectivity may be different even when a same subject watched a same movie twice (e.g., Cui et al., 2021).

We thank the reviewer for the suggestion and agree that it would be fascinating if the predictions can be made with high fidelity in neuropsychological populations. Although we are optimistic that our algorithm is able to generalize across diverse populations, to date, no previous literature has provided empirical evidence to illustrate the effectiveness, including optimizations and special applications beyond typical brains. Besides the neuropsychological population, it would also be valuable to study the generalization across a broad age range, for example, from infants to the elderly. The brain changes across age both anatomically and functionally, so it is a challenge to predict functional topographies based on a normative group that only includes young participants. With all these potential applications in mind, future research is needed to illustrate the efficacy, build the pipeline, and construct the representative normative groups to meet the requirements of accurate individualized predictions in diverse populations.

In typical populations, although participants have great individual variabilities in their functional topographies, for instance, some participants have distinguishable patches of activations in their left ventral temporal cortex while some participants don’t, our algorithms successfully captured these individualized differences in the prediction. The figure below shows, as an example, the face-selective topographies of two individuals that have markedly different face-selective topographies on the left ventral temporal cortex. The left participant has prominent face-selective areas on the left ventral temporal cortex that are in similar sizes as the right side, while the right participant only has a few scattered small face-selective spots on the left side. No matter what their face-selective areas look like, our algorithm accurately recovered the individualized locations, shapes, and sizes, retaining the individual variability in the functional topographies.

Functional connectivity profiles based on naturalistic stimuli are very stable across the cortex, even when participants watch different movies. In Figure 4-figure supplement 9, the mean correlations of fine-scaled connectome for most searchlights (r = 15mm) when participants watched The Grand Budapest Hotel and the Raiders of the Lost Ark were generally around 0.8. The mean correlations were about 0.9 between the first and second half of the same movie although the stimuli contents were different between the two halves. Thus, the fine-grained functional connectivity profiles remain highly stable and reliable across movie contents, which contributes to the robustness of cross-movie, time, and other parameters (e.g., scanner models, scanning parameter) predictions using our algorithms.

We added a paragraph in the discuss section to address the concerns (page 18-19):

“This study successfully illustrated that accurate individualized predictions are both robust and applicable across a variety of conditions, including movie types, languages, scanning parameters, and scanner models. Importantly, the intricate connectivity profiles remain consistent even when participants view entirely different movies, as evidenced by Figure 4-figure supplement 9, reinforcing the prediction's stability in various scenarios. However, all four datasets in this study only included typical participants with anatomically intact brains. An unanswered question is whether individualized topographies of neuropsychological populations with atypical cortical function (e.g., developmental prosopagnosics) or with lesioned brains (e.g., acquired prosopagnosics) could also be accurately predicted using the hyperalignment-based methods. Up to now, as far as we know, no previous literature has investigated this question. Beyond neuropsychological groups, it is also valuable to investigate how well the predictions will be across a wide range of age, from infants to the elderly. Future research is essential to adapt our algorithms to diverse populations.”

Reviewer #2 (Public Review):

Guo and her colleagues develop a new approach to map the category-selective functional topographies in individual participants based on their movie-viewing fMRI data and functional localizer data from a normative sample. The connectivity hyperalignment are used to derived the transformation matrices between the participants according to their functional connectomes during movies watching. The transformation matrices are then used to project the localizer data from the normative sample into the new participant and create the idiosyncratic cortical topography for the participant. The authors demonstrate that a target participant's individualized category-selective topography can be accurately estimated using connectivity hyperalignment, regardless of whether different movies are used to calculate the connectome and regardless of other data collection parameters. The new approach allows researchers to estimate a broad range of functional topographies based on naturalistic movies and a normative database, making it possible to integrate datasets from laboratories worldwide to map functional areas for individuals. The topic is of broad interest for neuroimaging community; the rationale of the study is straightforward and the experiments were well designed; the results are comprehensive. I have some concerns that the authors may want to address, particularly on the details of the pipeline used to map individual category-selective functional topographies.

We thank the reviewer for the encouragement.

1) How does the length of the scan-length of movie-viewing fMRI affect the accuracy in predicting the idiosyncratic cortical topography? Similarly, how does the number of participants in the normative database affect the prediction of the category-selective topography? This information is important for the researchers who are interested in using the approach in their studies.

To investigate the influence of movie-viewing data length and the number of participants in the normative database on prediction performance, we systematically varied these parameters. Specifically, we altered the number of runs utilized in the analysis for both the normative and target data and experimented with varying the number of participants in the normative dataset using the Budapest and the Sraiders datasets. We have included a new Figure 4-figure supplement 5 to present a summary of these findings.

The results reveal that both within-dataset and between-dataset prediction performances are positively correlated with the length of movie-viewing fMRI data used for both the normative and target groups. A similar trend was observed with respect to the number of participants included in the normative dataset. It is important to highlight, though, that, even when analyzing as little as one run of movie-viewing data—roughly 10-15 minutes, our hyperalignment-based prediction performance was significantly higher than that achieved using traditional surface alignment. This held true even when the normative dataset included as few as five participants.

In summary, our results show that prediction performance generally improves with longer movie-viewing sessions and larger normative datasets. However, it is noteworthy that even with minimal data—10 minutes of movie-viewing and a small number of participants in the normative dataset—our algorithm still outperforms traditional surface alignment methods significantly.

We also added sentences in the discussion section (page 15):

“We investigated the influence of naturalistic movie length and the size of the training group on the prediction accuracy of individualized functional topographies. By incrementally increasing both the number of movie runs in the training and target dataset and the participants in the training group in the Budapest and Sraiders dataset, we observed enhanced prediction accuracy (Figure 4-figure supplement 5). Notably, even with just one movie run in the training or target dataset, or with a mere five participants in the training group, our prediction performance (Pearson r) ranged from about 0.6 to 0.7. This accuracy significantly outperformed results obtained using surface-based alignment.”

2) The data show that category-selective topography can be accurately estimated using connectivity hyperalignment, regardless of whether different movies are used to calculate the connectome and regardless of other data collection parameters. I'm wondering whether the functional connectome from resting state fMRI can do the same job as the movie-watching fMRI. If it is yes, it will expand the approach to broader data.

We agree with the reviewer that demonstrating the applicability of the resting state data will expand the application scenarios of this approach. Most previous findings on resting state connectivity, including the comparison between the naturalistic and the resting state paradigms, focused on the macro-scale similarities and differences (e.g., Samara et al., 2023). Very few studies have investigated the fine-scaled connectome based on resting state data. The study on connectivity hyperalignment (Guntupalli et al., 2018) demonstrated a shared fine-scale connectivity structure among individuals that co-exists with the common coarse-scale structure and built the algorithm to successfully hyperalign individuals to the shared fine-scaled space. Another study from our lab (Feilong et al., 2021) revealed that the fine-scaled connectivity profiles in both resting and task states are highly predictive of general intelligence, indicating reliable and biologically relevant fine-scaled resting state connectome structures. Thus, it is highly plausible that our approach is able to be generalized to the resting state data, generating significantly better predictions of individualized functional topographies than traditional surface alignment. However, due to the limitations of the current datasets, we do not have resting state data available in the current datasets to perform this analysis. We are in the process of collecting new data to explore this hypothesis in future work.

We added sentences to the discussion section to discuss this idea (page 18):

“Studies comparing movie-viewing and resting state functional connectivity have shown that both paradigms yield overlapping macroscale cortical organizations (29), though naturalistic viewing introduces unique modality-specific hierarchical gradients. However, there remains a gap in research comparing the fine-scaled connectomes of naturalistic and resting state paradigms. Guntupalli and colleagues (14) revealed a shared fine-scale structure that coexists with the coarse-scale structure, and connectivity hyperalignment successfully improved intersubject correlations across a wide variety of tasks. Feilong et al. (13) noted that the fine-scaled connectivity profiles in both resting and task states are highly predictive of general intelligence. This suggests a reliable and biologically relevant fine-scale resting state connectivity structure among individuals. Therefore, it is plausible that individualized functional topography could be effectively estimated using resting state functional connectivity, expanding the applicability of our approach. Future studies are needed to explore this direction.”

3) The authors averaged the hyper-aligned functional localizer data from all of subjects to predict individual category-selective topographies. As there are large spatial variability in the functional areas across subjects, averaging the data from many subjects may blur boundaries of the functional areas. A better solution might be to average those subjects who show highly similar connectome to the target subjects.

We appreciate the reviewer’s insightful question about optimizing prediction performance by selecting participants most similar in functional connectivity to the target individuals. This is a promising direction and difficult problem as well. Our approach is based on fine-scale connectome to hyperalign participants, thus different groups of participants may be similar to the target participant in different searchlights. In addition, based on results discussed in the response to Q2, the more participants included in the normative dataset, the better the prediction performance. Thus, there is a trade-off between the number of participants included in the normative dataset for the prediction and the overall similarity of those participants to the target participant.

To quantitatively explore this idea, we used a searchlight in the right ventral temporal cortex, roughly at the location of posterior fusiform face area (pFFA).We sorted participants by their connectome similarity to each target participant and then examined prediction performance based on either the top nine most similar participants or the bottom nine least similar participants. Our results, presented in Figure 4-figure supplement 8, reveal that hyperalignment consistently outperforms surface alignment regardless of the subset of participants used. Notably, using the nine most similar participants did not significantly alter prediction performance (Tukey Test, z = -0.09, p = 0.996), while using the least similar participants did negatively impact it (Tukey Test, z = 2.492, p = 0.034). Interestingly, the stability of hyperalignment-based predictions remained high even when only a subset of participants was used, contrasting with the variability observed in surface-alignment-based predictions.

Overall, these findings suggest that while selecting functionally similar participants is a promising avenue for future optimization, the process will require nuanced, searchlight-specific criteria. Each searchlight may necessitate its own set of optimal participants to balance between the performance boost from having more participants and the fidelity gained from participant similarity.

We added the following to the discussion in the manuscript (page 16):

“In our study, we used fine-scale connectomes, noting that some participants are more similar to the target participant in specific searchlights. It is an interesting question whether predictions could be enhanced by exclusively selecting those more similar participants for the target participant. To explore this option, we examined a searchlight in the right ventral temporal cortex that was roughly at the location of the posterior fusiform area (pFFA) using the top and bottom nine participants similar to each target participant measured by their fine-scale connectome similarities in the budapest dataset. Generally, using all or part of the participants for the prediction generated similar results (Figure 4-figure supplement 8). Compared to using all the participants, using only the top nine participants who are the most similar to the target participants did not significantly improve the prediction (Tukey Test, z = -0.09, p = 0.996), but using only the bottom nine participants generated significantly lower prediction accuracies (Tukey Test, z = 2.492, p = 0.034). This suggests a trade-off between the number of participants included in the prediction and the similarity of the participants. Future studies are needed to explore the optimal threshold for the number of participants included for each searchlight to refine the algorithm.”

4) It is good to see that predictions made with hyperalignment were close to and sometimes even exceeded the reliability values measured by Cronbach's alpha. But, please clarify how the Cronbach's alpha is calculated.

Cronbach’s alpha calculates the correlation score between localizer-based maps across the runs, and it reflects the amount of noise in maps based on individual localizer runs. Traditionally, the reliability was estimated based on split-half correlations. For example, Guntupalli et al. (2016) used correlations of category-selectivity maps between odd and even localizer runs as the measure of reliability. The odd/even split measure underestimated reliability and necessitated recalculation of correlations between maps for only half the data to provide valid comparisons. In contrast, Cronbach’s alpha involves all localizer runs and provides a more accurate statistical estimate of the reliability of the topographies estimated with localizer runs.

Cronbach’s alpha has been used in many previously published works from our lab (e.g., Feilong et al., 2021; Jiahui et al., 2020, 2023). The code for implementing this metric is publicly accessible on the first author’s Github repository (https://github.com/GUOJiahui/face_DCNN/blob/main/code/cronbach_alpha.py).

We added the detailed explanation above to the Material and Methods section (page 24):

“Cronbach’s alpha calculates the correlation score between localizer-based maps across the runs, and it reflects the amount of noise in maps based on individual localizer runs. Traditionally, the reliability was estimated based on split-half correlations. The common odd/even split measure underestimated reliability and necessitated recalculation of correlations between maps for only half the data to provide valid comparisons. In contrast, Cronbach’s alpha involves all localizer runs and provides a more accurate statistical estimate of the reliability of the topographies estimated with localizer runs.”

5) Which algorithm was used to perform surface-based anatomical alignment? Can the state-ofthe-art Multimodal Surface Matching (MSM) algorithm from HCP achieve better performance?

We preprocessed our datasets using fMRIPrep, which employs algorithms from FreeSurfer’s recon-all for surface-based anatomical alignment. It is worth noting that different alignment methods can yield varying degrees of performance. For instance, a study by Coalson et al. (2018) compared the localization performance of multiple surface-based alignment methods, including Multimodal Surface Matching (MSM) and FreeSurfer. The study found that MSM outperformed FreeSurfer in terms of peak probabilities and spatial clustering, suggesting better overall localization.

Additionally, Guntupalli et al. (2018) evaluated intersubject correlations (ISC) of functional connectivity from movie-viewing data using both Connectivity Hyperalignment (CHA) and MSM-All with the Human Connectome Project (HCP) dataset. The study showed that although MSM-All yielded marginally better ISC than traditional surface alignment, CHA’s performance was significantly superior.

In summary, while using a more advanced alignment algorithm like MSM could marginally improve prediction performance, its advantages may not be substantial when compared to our CHA-based predictions. The combination of MSM and CHA represents an intriguing direction for future research, although it falls outside the scope of our current study.

6) Is it necessary to project to the time course of the functional localizer from the normative sample into the new participants? Does it work if we just project the contrast maps from the normative samples to the new subjects?

It is an interesting question and a practical alternative to researchers to know whether time series of the localizer runs are required to obtain reasonable predictions, as in some scenarios, contrast maps may be the only accessible data in the analysis. To quantitatively explore this possibility, we applied transformation matrices derived from the movie data to training participants’s individual pre-calculated contrast maps of all four categories, and evaluated the predictions. We found nearly similar prediction performance between the two flavors within and across datasets (Figure 4-figure supplement 7). However, it is worth noting that applying transformation matrices directly to contrast maps did not get as much improvement in the interactive steps as the other flavor in the advanced CHA, perhaps due to the scale changes when multiple iterations were implemented and the difficulty to properly normalize the t-maps compared to the regular time series.

Overall, although our algorithm is originally designed to be used on the time course of the functional localizer runs, relatively comparable results can be generated even when the contrast maps are directly projected from the normative group to the target participant. However, to derive the best results with our approach, time series are recommended when the situation permits.

We have also added the contents into the Discussion section (page 16):

“Our original algorithm is designed to apply transformation matrices to the time series of localizer data of training participants before generating contrast maps. To explore whether directly applying these matrices to pre-calculated contrast maps yields comparable results, we conducted an additional analysis across the four categories. Our findings indicate that the prediction outcomes were indeed quite similar between the two approaches for both the within- and across-datasets predictions (Figure 4-figure supplement 7). However, it is worth noting that the improvements observed with enhanced CHA were not as pronounced when applied directly to the contrast maps as opposed to the time series.”

7) Saygin and her colleagues have demonstrated that structural connectivity fingerprints can predict cortical selectivity for multiple visual categories across cortex (Osher DE et al, 2016, Cerebral Cortex; Saygin et al, 2011, Nat. Neurosci). I think there's a connection between those studies and the current study. If the author can discuss the connection between them, it may help us understand why CHA work so well.

We thank the reviewer for raising this point that provides us with the chance of clarifying how our approach differs with methods previously reported in the literature. The computational logic underlying our approach is that we derived the transformation matrices between the training and the target participants in the high-dimensional space based on functional connectivity calculated from the movie data. Then, we applied these transformation matrices to the training participant’s localizer data to accomplish the prediction. On the other hand, Saygin and colleagues directly used diffusion-weighted imaging (DWI) data and predicted participants’ functional responses based on the anatomical-functional correspondence. They evaluated the prediction by calculating the mean absolute errors (AE) of the difference between the actual and predicted contrast responses. Although AE linearly increases with the quality of the prediction, it is difficult to measure the prediction performance of the shape, size, and location of the functional areas precisely using this mean value. With our algorithm, we were able to predict the general location and size of the areas and recover the individualized shapes, generating more powerful predictions. We also used the searchlight analysis to evaluate the performance across the cortex systematically. In addition, Osher et al. (2016) and Saygin et al. (2012) always have a few participants failing to show better predictions based on the connectivity than the group averaged method. Our algorithm is more stable, as all participants across all four datasets had better predicted performance using our algorithm than using the group average. However, although we did not directly use the anatomical-functional correspondence with DWI, the relationships between individual structural connectivity and cortical visual category selectivity could be one of the biological underpinnings that contribute to this robust and accurate prediction.

The Connectivity-Based Shared Response Model (cSRM, Nastase et al., 2020) offers an alternative framework for aligning individuals through functional connectivity. While the overarching aim of cSRM and our methodology converges, substantial differences emerge in the respective implementation and application between the two methods that make our approach the more suitable for predicting individualized topographies. The most significant difference between the two is that, instead of focusing on within-individual connectivity profiles, cSRM used inter-subject functional connectivity (ISFC) in the initial step. This design requires that all participants must have time-locked time series, making the algorithm unusable for cross-content prediction and making it incompatible with resting-state data. Our approach, on the other hand, does not require time-locked stimuli, thereby offering a more flexible framework that permits generalization across different types of stimuli and experimental settings and enables bringing data across laboratories across the world together. Secondly, cSRM predominantly focuses on Region of Interest (ROI) analyses, whereas our model employs searchlight-based analyses designed to comprehensively cover the entire cortical sheet. Whole-brain coverage is needed to generate the topography that reflects the patterns across the cortex. Finally, with the optimized 1step method, our approach directly hyeraligns the training and target participants together, avoiding the accumulation of errors from the intermediate common space. cSRM, with an implementation similar to the classic connectivity hyperalignment, creates and hyperaligns all participants to a shared information space. In summary, while our approach and cSRM share a similar theoretical foundation, our approach has been specifically optimized to address the challenges and complexities in predicting individualized whole-brain functional topographies. Moreover, our approach demonstrates a remarkable ability to generalize across a variety of contexts and stimuli, offering a significant advantage in dealing with diverse experimental settings and datasets.

We have added the contents to the discussion section (page 16-17):

“By leveraging transformation matrices obtained from hyperaligning participants based on movie-viewing data, we successfully mapped these relationships to the training participants’ localizer data, enabling robust predictions. Prior work employing diffusion-weighted imaging (DWI) has underscored the link between anatomical connectivity and category selectivity across diverse visual fields (22, 23) and has established a notable congruence between structural and functional connectivities (24). These findings suggest that the unique anatomical connectivity patterns of individuals may serve as a foundational mechanism, contributing to the stable finescale functional connectome that underpins our approach. The connectivity-based Shared Response Model (cSRM) proposed by Nastase and colleagues (25) used connectivity to functionally align individuals similar to the connectivity hyperalignment algorithm. While both approaches share overarching goals, they diverge considerably in implementation and application. First and most important, cSRM used inter-subject functional connectivity (ISFC) rather than within-subject functional connectivity to initially estimate the connectome. As a result, cSRM requires participants to have time-locked fMRI time series. Therefore, unlike our algorithm, the cSRM approach does not support cross-content applications and also is not suitable for use with resting-state data. Second, cSRM is implemented based on a predefined cortical parcellation rather than the overlapping, regularly-spaced cortical searchlights applied in our method which are not constrained by areal borders. For the application, cSRM has mainly been used to do ROI analysis rather than the estimation of the whole-brain topography that requires broader coverage of the cortex with a searchlight analysis. Third, our method is specifically designed to work in each individual’s space, while cSRM decomposes data across subjects into shared and subjectspecific transformations, focusing on a communal connectivity space. In summary, although cSRM presents a promising alternative for similar aims, its current implementation precludes it from fulfilling the range of applications for which our method is optimized.”

Reviewer #3 (Public Review):

In this paper, Jiahui and colleagues propose a new method for learning individual-specific functional resonance imaging (fMRI) patterns from naturalistic stimuli, extending existing hyperalignment methods. They evaluate this method - enhanced connectivity hyperalignment (CHA) - across four datasets, each comprising between nine (Raiders) and twenty (Budapest, Sraiders) participants.

The work promises to address a significant need in existing functional alignment methods: while hyperalignment and related methods have been increasingly used in the field to compare participants scanned with overlapping stimuli (or lack thereof, in the case of resting state data), their use remains largely tied to naturalistic stimuli. In this case, having non-overlapping stimuli is a significant constraint on application, as many researchers may have access to only partially overlapping stimuli or wish to compare stimuli acquired under different protocols and at different sites.

It is surprising, however, that the authors do not cite a paper that has already successfully demonstrated a functional alignment method that can address exactly this need: a connectivitybased Shared Response Model (cSRM; Nastase et al., 2020, NeuroImage). It would be relevant for the authors to consider the cSRM method in relation to their enhanced CHA method in detail. In particular, both the relative predictive performance as well as associated computational costs would be useful for researchers to understand in considering enhanced CHA for their applications.

We thank the reviewer for raising this point that provides us with the chance of clarifying how our approach differs with methods previously reported in the literature. The computational logic underlying our approach is that we derived the transformation matrices between the training and the target participants in the high-dimensional space based on functional connectivity calculated from the movie data. Then, we applied these transformation matrices to the training participant’s localizer data to accomplish the prediction. On the other hand, Saygin and colleagues directly used diffusion-weighted imaging (DWI) data and predicted participants’ functional responses based on the anatomical-functional correspondence. They evaluated the prediction by calculating the mean absolute errors (AE) of the difference between the actual and predicted contrast responses. Although AE linearly increases with the quality of the prediction, it is difficult to measure the prediction performance of the shape, size, and location of the functional areas precisely using this mean value. With our algorithm, we were able to predict the general location and size of the areas and recover the individualized shapes, generating more powerful predictions. We also used the searchlight analysis to evaluate the performance across the cortex systematically. In addition, Osher et al. (2016) and Saygin et al. (2012) always have a few participants failing to show better predictions based on the connectivity than the group averaged method. Our algorithm is more stable, as all participants across all four datasets had better predicted performance using our algorithm than using the group average. However, although we did not directly use the anatomical-functional correspondence with DWI, the relationships between individual structural connectivity and cortical visual category selectivity could be one of the biological underpinnings that contribute to this robust and accurate prediction.

The Connectivity-Based Shared Response Model (cSRM, Nastase et al., 2020) offers an alternative framework for aligning individuals through functional connectivity. While the overarching aim of cSRM and our methodology converges, substantial differences emerge in the respective implementation and application between the two methods that make our approach the more suitable for predicting individualized topographies. The most significant difference between the two is that, instead of focusing on within-individual connectivity profiles, cSRM used inter-subject functional connectivity (ISFC) in the initial step. This design requires that all participants must have time-locked time series, making the algorithm unusable for cross-content prediction and making it incompatible with resting-state data. Our approach, on the other hand, does not require time-locked stimuli, thereby offering a more flexible framework that permits generalization across different types of stimuli and experimental settings and enables bringing data across laboratories across the world together. Secondly, cSRM predominantly focuses on Region of Interest (ROI) analyses, whereas our model employs searchlight-based analyses designed to comprehensively cover the entire cortical sheet. Whole-brain coverage is needed to generate the topography that reflects the patterns across the cortex. Finally, with the optimized 1step method, our approach directly hyeraligns the training and target participants together, avoiding the accumulation of errors from the intermediate common space. cSRM, with an implementation similar to the classic connectivity hyperalignment, creates and hyperaligns all participants to a shared information space. In summary, while our approach and cSRM share a similar theoretical foundation, our approach has been specifically optimized to address the challenges and complexities in predicting individualized whole-brain functional topographies. Moreover, our approach demonstrates a remarkable ability to generalize across a variety of contexts and stimuli, offering a significant advantage in dealing with diverse experimental settings and datasets.

We have added the contents to the discussion section (page 16-17):

“By leveraging transformation matrices obtained from hyperaligning participants based on movie-viewing data, we successfully mapped these relationships to the training participants’ localizer data, enabling robust predictions. Prior work employing diffusion-weighted imaging (DWI) has underscored the link between anatomical connectivity and category selectivity across diverse visual fields (22, 23) and has established a notable congruence between structural and functional connectivities (24). These findings suggest that the unique anatomical connectivity patterns of individuals may serve as a foundational mechanism, contributing to the stable finescale functional connectome that underpins our approach. The connectivity-based Shared Response Model (cSRM) proposed by Nastase and colleagues (25) used connectivity to functionally align individuals similar to the connectivity hyperalignment algorithm. While both approaches share overarching goals, they diverge considerably in implementation and application. First and most important, cSRM used inter-subject functional connectivity (ISFC) rather than within-subject functional connectivity to initially estimate the connectome. As a result, cSRM requires participants to have time-locked fMRI time series. Therefore, unlike our algorithm, the cSRM approach does not support cross-content applications and also is not suitable for use with resting-state data. Second, cSRM is implemented based on a predefined cortical parcellation rather than the overlapping, regularly-spaced cortical searchlights applied in our method which are not constrained by areal borders. For the application, cSRM has mainly been used to do ROI analysis rather than the estimation of the whole-brain topography that requires broader coverage of the cortex with a searchlight analysis. Third, our method is specifically designed to work in each individual’s space, while cSRM decomposes data across subjects into shared and subjectspecific transformations, focusing on a communal connectivity space. In summary, although cSRM presents a promising alternative for similar aims, its current implementation precludes it from fulfilling the range of applications for which our method is optimized.”

With this in mind, I noted several current weaknesses in the paper:

First, while the enhanced CHA method is a promising update on existing CHA techniques, it is unclear why this particular six step, iterative approach was adopted. That is: why was six steps chosen over any other number? At present, it is not clear if there is an explicit loss function that the authors are minimizing over their iterations. The relative computational cost of six iterations is also likely significant, particularly compared to previous hyperalignment algorithms. A more detailed theoretical understanding of why six iterations are necessary-or if other researchers could adopt a variable number according to the characteristics of their data-would significantly improve the transferability of this method.

In the advanced connectivity hyperalignment implementation, we gradually increased the number of targets. The six steps were not intentionally chosen but were the result of the increase to the maximum number of fine-grained targets, namely single cortical vertices.

Our datasets were resampled to the cortical mesh with 18,742 vertices across both hemispheres (approximately 3 mm vertex spacing; icoorder 5; 20,484 vertices before removing non-cortical vertices). Step 1 was the classic standard connectivity hyperalignment implementation based on the anatomically-aligned data. Since using dense connectivity targets (e.g., using all 18742 vertices on the surface) with anatomically-aligned data generates poor functional correspondence across participants (Busch et al., 2021), we used 1,284 vertices (icoorder 3, before removing the medial wall) as connectivity targets in step 1. However, it is beneficial to include more targets for calculating connectivity patterns after the first iteration of connectivity hyperalignment and repeated iterations to lead to a better solution by gradually aligning the information at finer scales. To better align across participants, we iterated the alignment for another two times (step 2 and step 3) with the same number of 1,284 coarse connectivity targets to ensure improved alignment before increasing the number of targets in the later steps. In step 4, we increased the number of targets to 5,124 (icoorder 4, before removing the medial wall), and iterated with this number of vertices for two times in total (step 4 & step 5) before using all vertices as targets. In the final step (step 6), all vertices were used as connectivity targets.

It is true that the multiple iteration steps largely increased the computational complexity compared to the classic connectivity hyperalignment, but the prediction increase was steady across all datasets and became comparable to response hyperalignment performance which requires time-locked stimuli. We did not use an explicit loss function in the algorithm, but followed the natural progression of the number of potential connectivity targets in the implementation. On the other hand, the difference between the performance of the improved and the classic connectivity hyperalignment was relatively small (difference of r < 0.05), which indicates the effectiveness of our classic algorithm. It is up to the researchers’ own options to adopt the number of iterations and the pace of increasing the number of targets in each step. If computational resources are limited or if a shorter total computational time is the primary priority, using the classic connectivity hyperalignment may be the best option to balance the trade-offs.

The Materials and Methods section had the details of the implementation (page 22-23):

“Using dense connectivity targets (e.g., using all 18742 vertices on the surface) with anatomically-aligned data usually generates poor functional correspondence across participants (33). It is, however, beneficial to include more targets for calculating connectivity patterns after the first iteration of connectivity hyperalignment and repeated iterations to lead to a better solution by gradually aligning the information at finer scales.

We used six steps to further improve the connectivity hyperalignment method. Step 1 was the initial connectivity hyperalignment step as described above that was based on the raw anatomically aligned movie data. The resultant transformation matrices were applied to those movie runs, and the hyperaligned data were then used in step 2 to calculate new connectivity patterns and calculate new transformation matrices. We repeated this procedure iteratively six times and derived transformation matrices for each step. In steps 1, 2, and 3, 642 × 2 (icoorder3, before removing the medial wall) connectivity targets were defined with 13 mm searchlights. In step 4 and 5, 2562 × 2 (icoorder 4, before removing the medial wall) connectivity targets were used with 7 mm searchlights to calculate target mean time series. In the final step 6, all 18742 vertices were included as separate connectivity targets, using each vertex’s time series rather than calculating the mean in a searchlight. Each step of this advanced connectivity hyperalignment algorithm increased the prediction performance (Figure 4-figure supplement 2).”

But to help the readers understand the logic of the advanced connectivity hyperalignment algorithm used in this study, we expanded the discussion section (page 15):

“Because using dense connectivity targets (e.g., using all vertices as connectivity targets) with anatomically-alignment data often leads to suboptimal alignment across participants (33), we started with coarse connectivity targets and gradually increased the number of connectivity targets to form a denser representation of connectivity profiles. The iterations improved the prediction performance step by step, and at the final step (step 6, all vertices were used as connectivity targets) in this analysis, the enhanced CHA generated comparable performance with RHA (Figure 4-figure supplement 4).”

Second, the existing evaluations for enhanced CHA appear to be entirely based on imagederived correlations. That is, the authors compare the predicted image from CHA with the ground-truth image using correlation. While this provides promising initial evidence, correlation-based measures are often difficult to interpret given their sensitivity to image characteristics such as smoothness. Including Cronbach's alpha reliability as a baseline does not address this concern, as it is similarly an image-based statistic. It would be useful to see additional predictive experiments using frameworks such as time-segment classification, intersubject decoding, or encoding models.

We appreciate the reviewer’s concern regarding the stability of local correlations in relation to image characteristics. To address this, we conducted additional analysis using different searchlight sizes (with radii of 10 mm, 15 mm, and 20 mm) to evaluate the predicted categoryselective maps, focusing specifically on the Budapest dataset. The local correlations between the predicted category-selective maps (obtained using enhanced CHA) and participants’ own maps based on classic localizer runs were calculated for each searchlight. We averaged these correlations across participants and plotted the resulting maps, as shown in Figure 4-figure supplement 10. Although using a larger searchlight radius is similar to employing a larger smoothing kernel, the results remained relatively stable across different searchlight sizes, particularly in regions selectively responsive to the specific category. This stability suggests that while the evaluation may be influenced by image-related features, the conclusion would remain consistent under varying parameters.

As for the use of enhanced CHA, it serves as an optimized version of the classic CHA, specifically designed for predicting individualized functional topographies. Evaluating prediction performance in our study is based on t-value contrast maps for each participant. Given this, it's unclear how time-segment classification or other decoding/encoding models could be appropriately implemented for performance evaluation. However, prior research from our lab has already established the effectiveness of classic CHA. Specifically, Guntupalli et al. (2018) showed that classic CHA significantly improved intersubject correlations (ISC) of connectivity profiles across the cortex. They also revealed that CHA captured fine-scale variations in connectivity profiles for nearby cortical nodes across participants and led to improved betweensubject multivariate pattern classification accuracies (bsMVPC) of movie segments. These findings serve as robust evidence for the effectiveness of classic CHA, laying the groundwork for our enhanced CHA approach.

We added Figure 4-figure supplement 10 to the supplementary material:

Addressing these concerns and considering cSRM as a comparison model would significantly strengthen the paper. There are also notable strengths that I would encourage the authors to further pursue. In particular, the authors have access to a unique dataset in which the same Raiders of the Lost Ark stimulus was scanned for participants within the Budapest (SRaiders) dataset as well as non-overlapping participants in the Raiders dataset. Exploring the relative performance for cross-movie prediction within a dataset as compared to a shared movie prediction across datasets is particularly interesting for methods development. I would encourage the authors to explicitly report results in this framework to highlight both this unique testing structure as well as the performance of their enhanced CHA method.

We appreciate the reviewer's suggestion to examine a shared time-series but non-overlapping participants scenario using the Sraiders and Raiders datasets. However, there are significant differences between the two datasets that preclude such direct comparison. These differences include varying scanning parameters, MRI scanners, localizer types, and data collection procedures. Due to these methodological divergences, the datasets cannot be treated as identical time-series.

Firstly, the scanning parameters vary considerably. Sraiders were scanned with TR = 1 s (TR/TE = 1000/33 ms, flip angle = 59 °, resolution = 2.5 mm3 isotropic voxels, matrix size = 96 × 96, FoV = 240 × 240 mm, multiband acceleration factor = 4, and no in-plane acceleration), and Raiders were scanned with TR = 2.5 s (TR = 2.5 s, TE = 35 ms, Flip angle = 90°, 80 × 80 matrix, FOV = 240 mm × 240 mm, resolution = 0.938 mm × 0.938 mm × 1.0 mm).

Secondly, participants in the Sraiders were scanned with a 3 T S Magnetom Prisma MRI scanner with a 32 channel head coil and the Raiders dataset, collected more than 10 years ago, used a 3T Philips Intera Achieva scanner with an eight-channel head coil.

Thirdly, the stimuli presentations were different. In the Sraiders dataset, the movie Raiders of the Lost Ark was split into eight parts (~15 min each), and the first four parts were watched outside of the scanner prior to the scanning (~56 min). The later four parts were watched in the scanner (57 min) with audio. And in the Raiders dataset, the audio-visual movie was split into eight parts (~15 min each). Participants watched all eight parts in the scanner with audio (one part / per run).

Fourthly and critically, the two datasets included two types of localizers. The Sraiders dataset included dynamic localizer runs, and the Raiders dataset only contained a static localizer that was similarly designed as in the Forrest dataset.

With all four points, it is not suitable to treat the two datasets as identical time-series. The difference in the localizer type is a further issue. The topographies generated from the two types of localizers are dissimilar in many ways. For all categories, the dynamic localizer elicited stronger and broader category-selective activations than the static localizer, and the searchlight analysis showed that the dynamic localizer had higher reliabilities across the cortex, especially in regions that were selectively responsive to the target category. Due to these differences, crossdataset predictions yielded lower correlations than within-dataset predictions. This is not indicative of methodological failure but reflects diverging topographies activated by different localizers.

In the manuscript, we have extensively analyzed cross-dataset predictions (Figure 2-figure supplement 1-Figure 4-figure supplement 4 & 6).

● Figure 2-figure supplement 1 demonstrates that, despite the limitations of cross-localizertype evaluation, both R-to-S (Raiders to Sraiders) and S-to-R (Sraiders to Raiders) predictions significantly outperformed surface alignment methods across categories.

● Figure Figure 2-figure supplement 2 confirms that the prediction performance remained stable across individual participants, underscoring the robustness of our methodology.

● Figure 3-figure supplement 1 & Figure 3-figure supplement 2 display contrast maps generated from both native and alternate localizers, revealing that the maps share similar topographies irrespective of the dataset origin.

● Figure 4-figure supplement 1 presents a correlation analysis of local similarities in R-to-S and S-to-R predictions, highlighting particularly strong correlations in the ventral face regions.

● Figure 4-figure supplement 2 employs histograms to showcase performance across major cortices and furnishes additional evidence regarding the influence of localizer types on the results.

● Figure 4-figure supplement 3 offers a searchlight analysis for other categories, enriching the scope of our investigation.

● Figure 4-figure supplement 4 affirms that the advanced CHA is effective in both R-to-S and S-to-R predictions.

● Figure 4-figure supplement 6 compares the efficacy of 1-step vs. 2-step prediction methods for R-to-S and S-to-R, showing a clear advantage for the 1-step approach.

These analyses affirmed that our approach outperforms surface alignment methods. But the inherent limitations in data collection and localizer types preclude a direct exploration of the reviewer’s hypothesis. These complexities necessitate further research to fully validate the proposed scenario.

Overall, I share the authors' enthusiasm for the potential of cross-movie, cross-dataset prediction, and I believe that methods such as enhanced CHA are likely to significantly improve our ability to make these comparisons in the near future. At present, however, I find that the theoretical and experimental support for enhanced CHA is incomplete. It is therefore difficult to assess how enhanced CHA meets its goals or how successfully other researchers would be able to adopt this method in their own experiments.

We hope our new analysis and replies addressed the reviewer’s concerns.

Reviewer #2 (Public Review):

Guo and her colleagues develop a new approach to map the category-selective functional topographies in individual participants based on their movie-viewing fMRI data and functional localizer data from a normative sample. The connectivity hyperalignment are used to derived the transformation matrices between the participants according to their functional connectomes during movies watching. The transformation matrices are then used to project the localizer data from the normative sample into the new participant and create the idiosyncratic cortical topography for the participant. The authors demonstrate that a target participant's individualized category-selective topography can be accurately estimated using connectivity hyperalignment, regardless of whether different movies are used to calculate the connectome and regardless of other data collection parameters. The new approach allows researchers to estimate a broad range of functional topographies based on naturalistic movies and a normative database, making it possible to integrate datasets from laboratories worldwide to map functional areas for individuals. The topic is of broad interest for neuroimaging community; the rationale of the study is straightforward and the experiments were well designed; the results are comprehensive. I have some concerns that the authors may want to address, particularly on the details of the pipeline used to map individual category-selective functional topographies.

1. How does the length of the scan-length of movie-viewing fMRI affect the accuracy in predicting the idiosyncratic cortical topography? Similarly, how does the number of participants in the normative database affect the prediction of the category-selective topography? This information is important for the researchers who are interested in using the approach in their studies.<br /> 2. The data show that category-selective topography can be accurately estimated using connectivity hyperalignment, regardless of whether different movies are used to calculate the connectome and regardless of other data collection parameters. I'm wondering whether the functional connectome from resting state fMRI can do the same job as the movie-watching fMRI. If it is yes, it will expand the approach to broader data.<br /> 3. The authors averaged the hyper-aligned functional localizer data from all of subjects to predict individual category-selective topographies. As there are large spatial variability in the functional areas across subjects, averaging the data from many subjects may blur boundaries of the functional areas. A better solution might be to average those subjects who show highly similar connectome to the target subjects.<br /> 4. It is good to see that predictions made with hyperalignment were close to and sometimes even exceeded the reliability values measured by Cronbach's alpha. But, please clarify how the Cronbach's alpha is calculated.<br /> 5. Which algorithm was used to perform surface-based anatomical alignment? Can the state-of-the-art Multimodal Surface Matching (MSM) algorithm from HCP achieve better performance?<br /> 6. Is it necessary to project to the time course of the functional localizer from the normative sample into the new participants? Does it work if we just project the contrast maps from the normative samples to the new subjects?<br /> 7. Saygin and her colleagues have demonstrated that structural connectivity fingerprints can predict cortical selectivity for multiple visual categories across cortex (Osher DE et al, 2016, Cerebral Cortex; Saygin et al, 2011, Nat. Neurosci). I think there's a connection between those studies and the current study. If the author can discuss the connection between them, it may help us understand why CHA work so well.

Author Response

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

Reviewer #1 (Public Review):

Soudi, Jahani et al. provide a valuable comparative study of local adaptation in four species of sunflowers and investigate the repeatability of observed genomic signals of adaptation and their link to haploblocks, known to be numerous and important in this system. The study builds on previous work in sunflowers that have investigated haploblocks in those species and on methodologies developed to look at repeated signals of local adaptations. The authors provide solid evidence of both genotype-environment associations (GEA) and genome-wide association study (GWAS), as well as phenotypic correlations with the environment, to show that part of the local adaptation signal is repeatable and significantly co-occur in regions harboring haploblocks. Results also show that part of the signal is species specific and points to high genetic redundancy. The authors rightfully point out the complexities of the adaptation process and that the truth must lie somewhere between two extreme models of evolutionary genetics, i.e. a population genetics view of large effect loci and a quantitative genetics model. The authors take great care in acknowledging and investigating the multiple biases inherent to the used methods (GEA and GWAS) and use a conservative approach to draw their conclusions. The multiplicity of analyses and their interdependence make them slightly hard to understand and the manuscript would benefit from more careful explanations of concepts and logical links throughout. This work will be of interest to evolutionary biologists and population geneticists in particular, and constitutes an additional applied example to the comparative local adaptation literature.

Some thoughts on the last paragraph of the discussion (L481-497): I think it would be fine to have some more thoughts here on the processes that could contribute to the presence/absence of inversions, maybe in an "Ideas and Speculation" subsection. To me, your results point to the fact that though inversions are often presented as important for local adaptation, they seem to be highly contingent on the context of adaptation in each species. First, repeatability results are only at the window/gene level in your results, the specific mutations are not under scrutiny. Is it possible that inversions are only necessary when sets of small effect mutations are used, opposite to a large effect mutation in other species? Additionally, in a model with epistasis, fitness effects of mutations are dependent on the genomic background and it is possible that inversions were necessary in only certain contexts, even for the same mutations, i.e. some adaptive path contingency. Finally, do you have specific demographic history knowledge in this system that maps to the observations of the presence of inversions or not? For example, have the species "using" inversions been subject to more gene flow compared to others?

Thank you for the great suggestions and helpful comments. Regarding the question of demography, each of the species actually harbours quite a large number of haploblocks (13 in H. annuus spanning 326Mb, 6 in H. argophyllus spanning 114 Mb, and 18 in H. petiolaris spanning 467 Mb; see Todesco et al. 2020 for more details) so there does not seem to be any clear association with demography. We agree about the complexities that might underly the evolution of inversions that you outline above, and have refined some of the text where we discuss their evolution in the Discussion.

Reviewer #2 (Public Review):

In this study the authors sought to understand the extent of similarity among species in intraspecific adaptation to environmental heterogeneity at the phenotypic and genetic levels. A particular focus was to evaluate if regions that were associated with adaptation within putative inversions in one species were also candidates for adaptation in another species that lacked those inversions. This study is timely for the field of evolutionary genomics, due to recent interest surrounding how inversions arise and become established in adaptation.

Major strengths

Their study system was well suited to addressing the aims, given that the different species of sunflower all had GWAS data on the same phenotypes from common garden experiments as well as landscape genomic data, and orthologous SNPs could be identified. Organizing a dataset of this magnitude is no small feat. The authors integrate many state-of-the-art statistical methods that they have developed in previous research into a framework for correlating genomic Windows of Repeated Association (WRA, also amalgamated into Clusters of Repeated Association based on LD among windows) with Similarity In Phenotype-Environment Correlation (SIPEC). The WRA/CRA methods are very useful and the authors do an excellent job at outlining the rationale for these methods.

Thank you!

Major weaknesses

The study results rely heavily on the SIPEC measure, but I found the values reported difficult to interpret biologically. For example, in Figure 4 there is a range of SIPEC from 0 to 0.03 for most species pairs, with some pairs only as high as ~0.01. This does not appear to be a high degree of similarity in phenotype-environment correlation. For example, given the equation on line 517 for a single phenotype, if one species has a phenotype-environment correlation of 1.0 and the other has a correlation of 0.02, I would postulate that these two species do not have similar evolutionary responses, but the equation would give a value of (1+0.02)10.02/1 = 0.02 which is pretty typical "higher" value in Figure 4. I also question the logic behind using absolute values of the correlations for the SIPEC, because if a trait increases with an environment in one species but decreases with the environment in another species, I would not predict that the genetic basis of adaptation would be similar (as a side note, I would not question the logic behind using absolute correlations for associations with alleles, due to the arbitrary nature of signing alleles). I might be missing something here, so I look forward to reading the author's responses on these thoughts.

The reviewer makes a very good point about the range of SIPEC, and we have changed our analysis to reflect this, now reporting the maximum value of SIPEC for each environment (across the axes of the PCA on phenotypes that cumulatively explain 95% of the variance), in Figure 4 and Supplementary Figures S2 and S13. For consistency among manuscript versions and to illustrate the effect of this change, we retain the mean SIPEC value in one figure in the supplementary materials (S12), which shows the small effect of this change on the qualitative patterns. Figure 4 now shows that the maximum SIPEC value is regularly quite strong, which should address the reviewer’s concern that this is not being driven by anomalous and small values. We appreciate this point and think this change now more closely reflects how we are trying to estimate the biological feature of interest – that some axis of phenotypic space is strongly (or not) responding to selection from the environmental variable.

With respect to the logic behind using absolute value, we still feel this is justified for traits, because if a trait evolves to be bigger or smaller, it may still use the same genes. For example, flowering time may change to be later or earlier, which would result in opposite correlations with a given environment, but might use the same gene (e.g. FT) for this. As such, we think keeping absolute value is more representative as otherwise species with strong but opposite patterns of adaptation would look like they were very different. We have added a statement on line 584 in the methods section to further clarify the reason for this choice.

An additional potential problem with the analysis is that from the way the analysis is presented, it appears that the 33 environmental variables were essentially treated as independent data points (e.g. in Figure 4, Figure 5). It's not appropriate to treat the environmental variables independently because many of them are highly correlated. For example in Figure 4, many of the high similarity/CRA values tend to be categorized as temperature variables, which are likely to be highly correlated with each other. This seems like a type of pseudo replication and is a major weakness of the framework.

This is a good point and we fully agree. It is for this reason that we didn’t present any p-values or statistical tests of the overall patterns that are shown in these figures (i.e. the linear relationship between SIPEC and number of CRAs in figure 4 and the tendency for most points to fall above the 1:1 line in figure 5). But to make sure this is even more clear, we have added statements to the captions of these figures to remind readers that points are non-independent. We still feel that in the absence of a formal test, the overall patterns are strongly consistent with this interpretation. A smaller number of non-pseudo-replicated points in Figure 4 would still likely show linear patterns. Similarly, there are almost no significant points falling below the 1:1 line in Figure 5, and it seems unlikely that pseudoreplication would generate this pattern.

Below I highlight the main claims from the study and evaluate how well the results support the conclusions.

"We find evidence of significant genome-wide repeatability in signatures of association to phenotypes and environments" (abstract)<br /> Given the questions above about SIPEC, I did not find this conclusion well supported with the way the data are presented in the manuscript.

We have changed the reporting of the SIPEC metric so that it more clearly reflects whichever axis of phenotypic space is most strongly correlated with environment in both species (using max instead of mean). This shows similar qualitative patterns but illustrates that this happens across much higher values of SIPEC, showing that it is in fact driven by high correlations in each species (or non-similar correlations resulting in low values of SIPEC). While we agree about the pseudo-replication problem preventing formal statistical test of this hypothesis, the visual pattern is striking and seems unlikely to be an artefact, so we think this does still support this conclusion.

"We find evidence of significant genome-wide repeatability in signatures of association to phenotypes and environments, which are particularly enriched within regions of the genome harbouring an inversion in one species. " (Abstract) And "increased repeatability found in regions of the genome that harbour inversions" (Discussion)<br /> These claims are supported by the data shown in Figure 4, which shows that haploblocks are enriched for WRAs. I want to clarify a point about the wording here, as my understanding of the analysis is that the authors test if haploblocks are enriched with WRAs, not whether WRAs are enriched for haploblocks. The wording of the abstract is claiming the latter, but I think what they tested was the former. Let me know if I'm missing something here.

We are actually not interested in whether WRAs are enriched for haploblocks; we want to know if WRAs tend to occur more commonly within haploblocks than outside of them. We have tried to clarify that this is our aim in various places in the manuscript. Our analysis for Figure 5 is the one supporting these claims, and it uses the Chi-square test statistic to assess the number of WRAs and non-WRAs that fall within vs. outside of inversions, and a permutation test to assess the significance of this observation, for each environmental variable and phenotype. We don’t think that this test has any direction to it – it’s simply testing if there is non-random association between the levels of the two factors. Thus, we think the wording we have used is consistent with the test result and our aims. Perhaps the confusion arose from the two methods that we present in the Methods (one is used for Figure 5, the other for Figure S6C & D), so we have added clarifications there.

Notwithstanding the concerns about highly correlated environments potentially inflating some of the patterns in the manuscript, to my knowledge this is the first attempt in the literature to try this kind of comparison, and the results does generally suggest that inversions are more likely capturing, rather than accumulating adaptive variation. However, I don't think the authors can claim that repeated signatures are enriched with haploblock regions, and the authors should take care to refrain from stating the relative importance of different regions of the genome to adaptation without an analysis.

Actually, we don’t have a strong feeling about whether inversions are capturing vs. accumulating adaptive variation, as these results could be consistent with either. As described above, we do not understand why we can’t claim that repeated signatures are enriched within haploblocks. We thought the reviewer is perhaps referring to the fact that the points are pseudo-replicated in the figures due to environment? We note that a very large number of points are significantly different from random in terms of the distribution of WRAs within vs. outside of haploblocks (light- vs. dark-shaded symbols), and that almost all of them fall above the 1:1 line. While there may be pseudo-replication preventing a test of the bigger multi-environment/multi-species hypothesis across all phenotypes and environments, there is almost a complete lack of significant results in the other direction. This seems like quite strong evidence about enrichment of WRAs within haploblocks, across many environments/species contrasts. We have added some text to the description of patterns in figure 5 to try to clarify this.

"While a large number of genomic regions show evidence of repeated adaptation, most of the strongest signatures of association still tend to be species-specific, indicating substantial genotypic redundancy for local adaptation in these species." (Abstract)<br /> Figure 3B certainly makes it look like there is very little similarity among species in the genetic basis of adaptation, which leaves the question as to how important the repeated signatures really are for adaptation if there are very few of them. (Is 3B for the whole genome or only that region?). This result seems to be at odds with the large number of CRAs and the claims about the importance of haploblock regions to adaptation, which extend from my previous point.

Figure 3B is for the whole genome, we have added text to the figure caption to clarify this. We think that both interpretations are possible: that most of the regions of the genome that are driving adaptation are non-repeated, but that a small but significant proportion of regions driving adaptation are repeated above what would be expected at random. Thus, it seems that there is high redundancy, coupled with adaptation via some genes that seem particularly functionally important and non-redundant, and therefore repeated. We added clarifying text on lines 541-548.

"we have shown evidence of significant repeatability in the basis of local adaptation (Figure 4, 5), but also an abundance of species-specific, non-repeated signatures (Figure 3)"<br /> While the claim is a solid one, I am left wondering how much of these genomes show repeated vs. non-repeated signatures, how much of these genomes have haploblocks, and how much overlap there really is. Finding a way to intuitively represent these unknowns would greatly strengthen the manuscript.

We agree, and really struggled to find the best way to communicate both the repeated patterns and the large amount of non-repeated signatures. Unfortunately, we have more confidence in the validity of repeated patterns because for the non-repeated patterns, a strong signature of association to environment in only one species could just be the product of structureenvironment correlation, as we didn’t control for population structure. Thus, trying to quantify the proportion of non-repeated signatures is difficult to do with any accuracy and we preferred to avoid putting too much emphasis on the simple calculation of the proportion of top candidate windows that were also WRAs.

Overall, I think the main claims from the study, the statistical framework, and the results could be revised to better support each other.

Although the current version of the manuscript has some potential shortcomings with regards to the statistical approaches, and the impact of this paper in its present form could be stifled because the biology tended to get lost in the statistics, these shortcomings may be addressed by the authors.

With some revisions, the framework and data could have a high impact and be of high utility to the community.

Thank you for your very helpful comments and suggestions on our paper, we really appreciate it.

Recommendations for the authors: please note that you control which revisions to undertake from the public reviews and recommendations for the authors

Editor's comments:

The reviewers make a series of reasonable suggestions that I echo. I found the paper quite hard to follow, and got fairly lost in the various layers of analyses done. Partially, this represents the complexity of empirical genomic data, which rarely deliver simple stories of convergence at a few genes. However, the properties of the various statistics used to detail local adaptation and convergence are not particularly clear and the figures presented were not intuitive representations of the data. This leaves the reader with an incomplete view of how much weight to put in the various lines of evidence marshaled. I would suggest simplifying the presentation of the results considerably. I add a few additional comments below.

Great suggestion, we’ve added a schematic overview of the methods and main research questions to Figure S1 in the supplementary materials.

A figure would help showing some of the signals of SNPs with putative signals of convergent environmental correlations across species, e.g. frequencies plotted against climate variables. This would help readers get a sense of how strong these signals were. These could be accompanied by the statistics calculated for these SNPs, that would allow the reader to start to get some intuitive sense of what the numbers mean.

Great suggestion, we have added a schematic overview of the methods to Figure S1 that shows some of the values and illustrates how the methods work using visual examples from our data.

In general, the introduction and some of the discussion of the inversion results feel oddly framed:<br /> Abstract line 36: "This shows that while inversions may facilitate local adaptation, at least some of the loci involved can still make substantial contributions without the benefit of recombination suppression."

We have changed “some of the loci involved can still make substantial contributions without the benefit of recombination suppression” here to “some of the loci involved can still harbour mutations that make substantial contributions without the benefit of recombination suppression in species lacking a segregating inversion” as it hopefully clarifies that we’re not talking about individual alleles that are present in both species.

Models of the role of local adaptation in the establishment of inversions (Kirkpatrick & Barton) assume that there are multiple locally adapted alleles already present. It is the load created by these alleles being constantly maintained in the face of migration and subsequent recombination that allow an inversion to be selected for because it keeps together locally adapted alleles. Thus these models predict that there could well be standing local adaptation at these loci in the absence of the inversion in other species, and that these locally adapted alleles while not fixed may be at high frequency. (After establishment, inversions housing locally adapted alleles, can shield more weakly, locally beneficial alleles from migration allow other alleles to build up.) Empirically it's interesting to find signals of local adaptation in other species that don't contain putative inversions. But the logic of the different predictions is not particularly clear from the introduction, and only becomes somewhat clearer in the discussion.

Thank you for pointing out this murkiness, we have re-written portions of both the Introduction and Discussion to clarify this aspect.

From the introduction: Inversions have been implicated in local adaptation in many species (Wellenreuther and Bernatchez 2018), likely due to their effect to suppress recombination among inverted and noninverted haplotypes, and thereby maintain LD among beneficial combinations of locally adapted alleles (Rieseberg 2001; Noor et al. 2001; Kirkpatrick and Barton 2006). This has been approached by models studying the establishment of inversions that capture combinations of locally adapted alleles present as standing variation (e.g., Kirkpatrick and Barton 2006), as well as models examining the accumulation of locally adapted mutations within inversions (e.g., Schaal et al. 2022). If there is variation in the density of loci that can potentially contribute to local adaptation, inversions would be expected to preferentially establish and be retained in regions harbouring a high density of such loci (and this expectation would hold for both the capture and accumulation models). We would also expect to see stronger signatures of repeated local adaptation in such high density regions. Despite mounting evidence of their importance in adaptation, it is unclear how inversions may covary with repeatability of adaptation among species. A fundamental parameter of importance in these models is the relationship between migration rate and strength of selection on individual alleles, which may not make persistent contributions to local adaptation without the suppressing effects of recombination if selection is too weak (Yeaman and Whitlock 2011; Bürger and Akerman 2011). If most alleles have small effects relative to migration rate and can only contribute to local adaptation via the benefit of the recombination-suppressing effect of an inversion, then we would expect little repeatability at the site of an inversion – other species lacking the inversion would not tend to use that same region for adaptation because selection would be too weak for alleles to persist. On the other hand, if some loci are particularly important for local adaptation and regularly yield mutations of large effect, with these patterns being conserved among species, repeatability within regions harbouring inversions may be substantial. Thus, studying whether adaptation at the same genomic region harbouring an inversion is observed in other species lacking the inversion can give insights about the underlying architecture of adaptation, and the evolution and maintenance of inversions.

From the Discussion: The observed repeatability associated with inversions further supports the local adaptation model as an explanation for the long-term persistence of segregating inversions (at least in sunflowers, rather than mechanisms based on dominance or meiotic drive (Rieseberg 2001). If there is variation across the genome in the density of loci with the potential to be involved in local adaptation, then the establishment and maintenance of inversions would be biased towards regions harbouring a high density such loci under this model. If the genomic basis for local adaptation is conserved amongst species, then these same regions are more likely to have high repeatability. Thus, our observation of genomic regions harbouring inversions also being enriched for WRAs is consistent with this general model for inversion evolution. Unfortunately, our observations do not provide much insight into whether inversions evolve through the capture (e.g. Kirkpatrick and Barton 2006) or accumulation (e.g. Schaal et al. 2022) type of model, as either model would be consistent with our results. Most of the sunflower inversions are >1 My old, and therefore predate any current local adaptation patterns, but likely do not predate the genes underlying local adaptation (which appear to be shared among the species we studied). As for the alleles underlying local adaptation, they may be younger than the inversions, but as our work suggests, these regions are prone to harbouring locally adaptive alleles so it is possible that they also harboured other ancestral locally adaptive alleles.

As a minor comment, there's a fair number of places where a more nuanced view of the field is needed, e.g.:<br /> "Models in evolutionary genetics tend to focus on extremes: population genetic approaches explore cases where strong selection deterministically drives a change in allele frequency" --This seems like a strange strawman. Population genetic models span a huge parameter range. The empirical approaches of looking for sweeps by detecting genome-wide statistical outliers is predicated on strong selection, but there are numerous papers that have looked for signals of weak selection genome-wide.

Good point, we have changed our wording here.

Reviewer #1 (Recommendations For The Authors):

Comments

My main comment on the manuscript is that the different levels and diversity of analyses are slightly hard to follow on the first, and even second, read. As there are several layers of correlations and comparisons, as well as some independent analyses, I wonder if it might be helpful to have a summary schematic figure of how all analyses fit together.

Great idea, we have added Figure S1 that summarizes the main flow of the methods and research questions.

• L169-171: Would it be more accurate to say that SIPEC is maximized when both species have strong correlations for an environmental variable across the same phenotypes? But maybe I misunderstood the index.

Good point, we have now simplified SIPEC, reporting the max instead of the mean, which we think better reflects when similar patterns are happening in both species for some phenotype.

• L191: Given the discussion in the introduction and elsewhere about the correction for population structure, which version is used here? Same for Figure 3.

We have added clarification there.

• L348: One [environmental] variable?

Added

• L353: Maybe add a percentage indication for 387 so that it is comparable to the following 23.3%.

Good point, added

-> L388 and paragraph: You mention "significant repeatability" but it is hard from the results at this point to have a broad idea of the amount of signal that is repeatable. Would it be possible to add here some quantitative measure of the proportion of signal repeatable or not, even if approximated?

I wish we could, but I think the precision implied by such an approximation would involve a huge amount of uncertainty and likely inaccuracy. Because it is so hard to conclusively identify how many loci are significant but non-repeated, we really don’t have a good handle on the denominator here. We are pretty confident that the repeated loci are strongly enriched for true positives, but the non-repeated loci are also almost certainly strongly enriched for false positives. While we really want to be able to quantify this explicitly, we don’t think it’s possible given our data.

-L415-418: "If there is variation [...] involved in local adaptation", I do not follow this argument, could you rephrase?

Changed

-L447-450: As you say in the supplementary methods, your analyses exclude 3/4 of the genome. Do you think this choice has a large impact on the number of outliers observed here as the genome-wide baseline would change?

This is a very good question, but one that is quite complex and without a clear answer – we chose not to delve into it in the paper to keep the discussion streamlined. My (SY) feeling is that it is unlikely that regions harbouring transposable elements would contribute much to adaptation, but I think we really don’t know if that is true. Even excluding ¾ of the genome harbouring TEs, ¼ of the genome still constitutes a huge amount of sequence and a very large number of genes and it seems plausible that most genes and genic regions would not contribute to adaptation for a given trait, so I don’t think this would change the results too much in a qualitative way – but would almost certainly change the number of windows that are significant, etc.

• L455-457: "As we are unable [...] potentially important drivers" Could you provide the logical link here between loci of small effect and them being important drivers. I presume you mean that the large effect loci found here only account for a small proportion of the heritability?

Yes that’s what we meant here, so we’ve added some clarification.

• L482: "enriched within inversions" should that be 'in genomic regions where there exist inversions in at least one species'? Thanks for catching that, yes. Changed.

• Methods/SIPEC L512: Compared to the Results section it is unclear here what is referred to as an "environment" Is it a variable or a set of environment variables?

This is done per environmental variable.

I find the presence of the PCA for environment variables in Figure 2 misleading as my first interpretation was that PCs for environment were also used.

Good point, we have clarified this on line 190-193.

Maybe one potential addition to the formula would be to add an environment variable $j$ notation such that it reads "$SIPEC_j = \sum_i (|r_{ij,1}| + ...) ...$ where ... between environment variable $j$". I had initial difficulties to understand how this SIPEC was computed relating to environmental variables and this might help.

Given the other changes we made to SIPEC, we felt it was simpler to just present it as a single calculation on a given combination of phenotype and environment for a pair of species, and then discuss taking the mean and maximum of this later.

Finally, PCA axes explaining 95% of the variance are used, I would find it interesting to see how many PCs are used in comparison to the number of traits being measured.

We have added the following sentence to the methods describing this:

"For comparisons including H. argophyllus, 95% of the variance was typically explained by 8-10 PC axes (out of 28 or 29 phenotypes), whereas for comparisons among other taxa this included 21 or 22 PC axes (out of 65 or 66 phenotypes."

Typos

L52: --

Changed

L254: portions [of] their

Changed

L399: additional closing parenthesis

Changed

L458: signatures [of] repeated association

Changed

L554: performed [on]

Changed

L578: 5 ~~kp~~/kb windows

Changed

L601: ~~casual~~/causal SNPs

Changed

L615: ~~widow~~/window

Changed

L732: ~~Banding~~/Banting Postdoctoral Fellowship

Changed

L1002 & L960: [Supplementary] Figure

Changed

Supplementary: Some figure titles are in bold and others are not.

Changed

Reviewer #2 (Recommendations For The Authors):

Overall I found the writing to be very clear and easy to follow. Despite my comments, it was clear that a lot of thought went into how to conduct the tests and visualize the results. I recommend ending the Discussion on a positive note, rather than an impossible test.

Thanks for the positive suggestion, we have done this.

In Figure 5, is the temperature variable missing in the legend and in the plot?

No, for this plot we just combined the temperature/precipitation variables into one variable called “climate”.

Author Response

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

Our comments on the initial eLife assessment

“This study presents a useful inventory of the joint effects of genetic and environmental factors on psychotic-like experiences, and identifies cognitive ability as a potential underlying mediating pathway. The data were analyzed using solid and validated methodology based on a large, multi-center dataset. The claim that these findings are of relevance to psychosis risk and have implications for policy changes are partially supported by the results”

We sincerely appreciate the editor and reviewers for their valuable feedback and their willingness to accommodate our perspectives in the first revision. In this revision, the comments from the reviewers have allowed us to further improve our manuscript. Regarding the eLife assessment, we would like to discuss two points.

Firstly, regarding your point of our “findings are of relevance to psychosis risk…partially supported…”, we want to address that our study is closely related to psychosis risk. Childhood psychotic-like experiences (PLEs) are closely linked to psychotic risk and have been shown to increase the risk of general psychopathology, as mentioned in our Introduction and Discussion.

The reviewers asked for clearer differentiation between PLEs and schizophrenia, which we incorporated in this revision (line 100~111; line 419~430). So, this revised version now clearly points out that findings are relevant primarily to psychosis risk, and only partially relevant to schizophrenia risk.

Secondly, regarding “…implications for policy changes are partially supported…”, we have revised our study’s social contribution more clearly and specifically. Incorporating the comments, we have revised that our study offers an insight to the future studies by showing the importance of integrative approaches, considering multi-factorial neurocognition and psychopathology ranging from genes to environment (line 503~512), rather than offers direct policy implications.

Our collaboration with eLife and the reviewers has proven satisfactory and enriching. The community, coupled with the innovative system and culture established around eLife, has significantly advanced the progression of scientific research. We are privileged to contribute to this endeavor.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I am happy with the revisions provided by the authors and I think most of my concerns have been addressed satisfactorily. One remaining concern is the authors' conflation of PLEs and schizophrenia. They stated, for example, that it is necessary to adjust for schizophrenia PGS. Even though studies have found a statistical relationship between schizophrenia PGS and PLEs, this relationship is not very strong (although statistically significant) and other studies have found no relationship. Similarly, having PLEs increases the risk of developing psychosis, but that does not necessarily mean that this risk is substantial or specific. I think this needs more nuance in the manuscript and the term 'schizophrenia' should be used sparsely and very carefully as the paper has focused on PLEs. Otherwise, great work on the revisions, thank you.

Thank you for your comment on the use of PLEs and schizophrenia. We clearly understand the differences between the two and we made relevant corrections throughout the manuscript. In particular, we added that PLEs are not a direct predictor of schizophrenia and corrected any expressions that may imply that PLEs are closely related to schizophrenia in the Introduction.

“Psychotic-like experiences (PLEs), which are prevalent in childhood, indicate the risk of psychosis (van der Steen et al., 2019; Van Os & Reininghaus, 2016). Although they are not a direct precursor of schizophrenia, children reporting PLEs in ages of 9-11 years are at higher risk of psychotic disorders in adulthood (Kelleher & Cannon, 2011; Poulton et al., 2000). PLEs also point towards the potential for other psychopathologies including mood, anxiety, and substance disorders (van der Steen et al., 2019), are linked to deficits in cognitive intelligence (Cannon et al., 2002; Kelleher & Cannon, 2011) and show a stronger association with environmental risk factors during childhood than other internalizing/externalizing symptoms (Karcher, Schiffman, et al., 2021).

Maladaptive cognitive intelligence may act as a mediator for the effects of genetic and environmental risks on the manifestation of psychotic symptoms (Cannon et al., 2000; Keefe et al., 2006; Reichenberg et al., 2005).” (line 100~111)

We also revised any expressions that could be perceived as implying relevance to schizophrenia in the Discussion. “Prior research identifying the mediation of cognitive intelligence focused on either genetic (Karcher, Paul, et al., 2021) or environmental factors (Lewis et al., 2020) alone. Studies with older clinical samples have shown that cognitive deficit may be a precursor for the onset of psychotic disorders (Eastvold et al., 2007; Fett et al., 2020; Vorstman et al., 2015). Our study advances this by demonstrating the integrated effects of genetic and environmental factors on PLEs through the cognitive intelligence in 9-11 years old children. Such comprehensive analysis contributes to assessing the relative importance of various factors influencing children's cognition and mental health, and it can aid future studies designed for identifying health policy implications. Considering the directions and magnitudes of the effects, though the effects of PGS remain significant, aggregated effects of environmental factors account for much greater degrees on PLEs.” (line 419~430)

Reviewer #2 (Recommendations For The Authors):

I thank the authors for addressing most of my comments. I feel the manuscript has already greatly improved.

I have a few more comments.

1) Although I did not make this comment, I find the authors' reply to the following comment by Reviewer #1 unclear: Original comment 'I like that the assessment of CP (cognitive performance) and self-reports PLEs is of good quality. However, I was wondering which 4 items from the parent-reported CBCL (Child Behavior Checklist) were used and how did they correlate with the child-reported PLEs? And how was distress taken into account in the child self-reported PLEs measurement? Which PLEs measures were used?'

The authors' response refers to correlation coefficients, but I think Reviewer #1's inquiry was on more than these correlations.

Thank you for your concern. We think that this comment was referring to our previous manuscript submitted elsewhere. In our initial submission to eLife, we already added the details about the four items from the parent-reported CBCL and how distress was considered in the child self-reported PLEs measurement (Appendix S1, page 48).

2) Regarding the authors' reply that they have 'standardized the use of 'cognitive capacity' - I do not understand what this means. How exactly was this term standardized? In fact, I can find the term 'cognitive capacity' only once and it seemed to have been deleted from the manuscript. This is fine, but it doesn't clearly align with the statement that this term has been standardized.

We apologize for causing such confusion. What we meant was that throughout our revised manuscript, we used the term “cognitive phenotypes” instead of “cognitive capacity”.

3) Regarding my initial comment that 'it needs to be described how cognitive performance was defined in Lee 2018.' - I believe this is still not clarified. The authors write 'CP was measured as the respondent's score on cognitive ability assessments', but it remains unclear what exactly these assessments were.

Thank you for pointing this out. We added that “CP, measured as the respondent's score on cognitive ability assessments of general cognitive function and verbal-numerical reasoning, was assessed in participants from the COGENT consortium and the UK Biobank” (line 204~206).

4) Regarding the authors' reply to my comment 'In the 'Path Modeling' section, please explain what 'factors and components' concretely refer to. How is this different from a standard SEM with latent factors?'

I can see that the authors explained 'components' (=the weighted sum of observed variables), but please also add what you mean by 'factors' - and how these are different from 'components' (line 284). Furthermore, I don't think it is correct that SEMs can only model latent factors, but not components (=measured variables). I also cannot see how using a weighted sum of observed variables controls more effectively for bias in estimation than latent factors. However, even though I do have some knowledge on this method, I'm not an expert and would appreciate the authors, other reviewer and/or editor to weigh in on this point.

Thank you for pointing this out. We added that latent factors are indirectly measured indicators that explain the covariance among observed variables (line 263~271). We also added that standard SEM method using latent factors assumes that observed variables within each construct share a common underlying factor, but if this assumption is not met, then the standard SEM method cannot effectively control for biases. This is the reason why the IGSCA method, which addresses this limitation by allowing for use of both composite and latent factors as constructs.

“Standard SEM using latent factors (i.e., indirectly measured indicators that explain the covariance among observed variables) to represent indicators such as PGS or family SES relies on the assumption that observed variables within each construct share a common underlying factor. If this assumption is violated, standard SEM cannot effectively control for estimation biases. The IGSCA method addresses this limitation by allowing for the use of composite indicators (i.e., components)—defined as a weighted sum of observed variables—as constructs in the model, more effectively controlling bias in estimation compared to the standard SEM. During estimation, the IGSCA determines weights of each observed variable in such a way as to maximize the variances of all endogenous indicators and components.” (line 263~271)

5) I overall disagree with the authors' following statement 'It has been suggested from prior studies that these variables (PGS, family SES, neighborhood SES, positive family and school environment, and PLEs) are less likely to share a common factor', but I appreciate the authors' argument.

Thank you for your comment. To make clarify our statement in the manuscript, we changed the sentence to “Considering that the observed variables of the PGSs, family SES, neighborhood SES, positive family and school environment, and PLEs are evaluated as a composite index by prior research, the IGSCA method can mitigate bias more effectively by representing these constructs as components” (line 274~277).

6) Regarding 'genetic ethnicity': please describe your methods on how this was defined.

Genetic ethnicity was defined as the genetic ancestry of participants, which is included as one of observations in the original ABCD Study data. To avoid further confusion, we corrected ‘genetic ethnicity’ to ‘genetic ancestry’ throughout the manuscript.

7) Regarding 'a more direct genetic predictor of PLEs' - I still don't understand what the contrast is here. More direct than what else?

The description was unclear; we removed it from our manuscript.

8) Regarding the factor loadings in Figure 3: I don't understand how deprivation loads positively on 'low neighborhood SES', but poverty loads negatively. Shouldn't they both show the same direction of effect/loading on neighbourhood SES, while 'years of residency' should show the opposite direction (i.e., deprivation and poverty = risk, while years of residency = protective)? Are these unexpected loadings?

The authors did not yet respond to this point: 'Please also add the autocorrelations between the 3 PLE measures. I assume these were also modelled statistically, given the strong correlations between time points?' Were these correlations not modelled? Why not?

Figure 3B is still unclear. Was intelligence included here? What is the difference between Figure 3A and B? The legend suggests that 3B shows the indirect effects, but figure 3B looks like a direct effect, while 3A seem to show the indirect effect.

The reviewer’s confusion resulted from our incorrect description. The factor loadings of low neighborhood SES were marked incorrectly. The loading for ‘years of residence’ and ‘poverty’ should be switched: -0.3648 for ‘years of residence’ and +0.877 for ‘poverty’. This was a mistake when we were applying factor loadings in the Figure. We thank you for pointing this out.

We apologize for missing your point on autocorrelation. Adding autocorrelations between the three PLEs is unrelated to our research goal. In this paper, we investigated how genetic and environmental factors explain the variations in PLEs between participants, regardless of changes over time. Since we used PLEs of multiple follow-ups to ensure that the results are robust irrespective of the timing of PLE measurements, taking autocorrelation into account is not necessary.

The decision to add autocorrelation, which involves using the outcome variable at time (t-1) as a predictor for the outcome variable at time t, depends on the research focus. If your interest lies in explaining inter-individual variation in the rate of change in PLEs over a one-year period, then autocorrelation should be controlled for (typically, predictors measured at different time points are used in such cases). However, this was not the focus of this paper, which is why we did not apply autocorrelation in the SEM analysis.

We apologize for the confusion between Figure 3A and 3B. To clarify, we added titles in the figure images as “Direct effects” and “Indirect effects”. We also changed the legend as well.

“A. Direct pathways from PGS, high family SES, low neighborhood SES, and positive environment to cognitive intelligence and PLEs. Standardized path coefficients are indicated on each path as direct effect estimates (significance level *p<0.05). B. Indirect pathways to PLEs via intelligence were significant for polygenic scores, high family SES, low neighborhood SES, and positive environment, indicating the significant mediating role of intelligence.” (line 968~973)

Figure 3A shows direct effects: i.e., the coefficients of paths from PGS, family SES, neighborhood SES, and positive environment to intelligence and PLEs, as well as the coefficient of paths from intelligence to PLEs. This is why Figure 3A shows colored arrows starting from PGS, family and neighborhood SES, and positive environment towards intelligence and PLEs, as well as the arrows from intelligence to PLEs. On the other hand, in Figure 3B, the colored arrows staring from PGS, family and neighborhood SES, and positive environment goes through intelligence, and heads towards PLEs. This was meant to show that the indirect effects shown in Figure 3B indicate the specific effects of PGS, family SES, neighborhood SES, and positive environment on PLEs mediated by intelligence.

In short, Figure 3 can be seen as a diagram drawn from Table 2: direct effects of the genetic and environmental variables on intelligence and PLEs, and direct effects of intelligence on PLEs are shown in Figure 3A; indirect effects of genetic and environmental variables on PLEs mediated by intelligence are shown in Figure 3B.

9) Regarding Supporting Information tables: to make these more digestible, I suggest using Excel and adding one table per sheet with a clear title and legend, indicating what each table shows. For example, Table S1 has 9(?) different subsections, all called the same (Linear Mixed Model: Multiethnic). It is not clear how each subsection differs from the others. Separate tables in separate excel sheets might be easier.

Also, I think two decimal points might be good enough, enhancing readability of these tables.

Thank you for your suggestion. We moved the supplementary tables into an external Excel file, with each sheet showing different tables, as well as titles, legends, and clear subsections.

10) Regarding reporting exact p-values in Table 2: I don't understand. At the moment, categorical significance statements are reported. Were these not based on exact p-values (or how else was it decided if a finding was significant at a 0.05 (?) significance level).

Either remove the significance column completely (as p-values cannot be estimated due to non-normality) or specify exactly/clarify what this column shows and this was derived.

We apologize for the confusion. In Table 2, we checked the significance of each path using 95% confidence intervals with 5,000 bootstrapping iterations. Since 95% confidence intervals that does not include zero is equivalent to p-values below 0.05 significance level, we believe this is an appropriate alternative for reporting the significance of each path in the SEM model.

We specified the reason why we were not able to calculate exact p-values (clean copy: line 299~303). “As a trade-off for obtaining robust nonparametric estimates without distributional assumptions for normality, the IGSCA method does not return exact p-values (Hwang, Cho, Jung, et al., 2021). As a reasonable alternative, we obtained 95% confidence intervals based on 5,000 bootstrap samples to test the statistical significance of parameter estimates.”

Author Response

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

Reviewer #1 (Public Review):

Summary:

This important study from Godneeva et al. establishes a Drosophila model system for understanding how the activity of Tif1 proteins is modified by SUMO. The authors nicely show that Bonus, like homologous mammalian Tif1 proteins, is a repressor, and that it interacts with other co-repressors Mi-2/NuRD and setdb1 in Drosophila ovaries and S2 cells. They also show that Bonus is SUMOylated by Su(var)2-10 on at least one lysine at its N-terminus to promote its interaction with setdb1. By combining nice biochemistry with an elegant reporter gene approach, they show that SUMOylation is important for Bonus interaction with setdb1, and that this SUMO-dependent interaction triggers high levels of H3K9me3 deposition and gene silencing. While there are still major questions of how SUMO molecularly promotes this process, this study is a valuable first step that opens the door for interesting future experimentation.

Major Point:

The RNAseq and ChIPseq data is not available. This is critical for the review of the paper and would help the readers and reviewers interpret the Bonus mutant phenotype and its mechanism of repressing genes.

The sequencing data have been deposited to the NCBI GEO archive. The accession number for all other RNA-seq and ChIP-seq data reported in this paper is GEO: GSE241375.

1) The author's conclusion that Bonus SUMOylation is "essential for its chromatin localization" is not supported by the data. Figure 5F shows less 3KR mutant in the chromatin fraction but there is still significant signal.

We appreciate the reviewer's feedback and agree that the term "essential" was not appropriate in this context. We have revised the manuscript to replace "essential" with "contributes to" to accurately reflect our findings.

2) The author's conclusion that Bonus is SUMOylated at a single site close to its N-terminus is not necessarily true. In several SUMO and Bonus blots throughout the paper (5B, 6C, S4A), there are >2 differentially migrating species that could represent more than one SUMO added to Bonus. While the single K20R mutation eliminates all of these species in Fig 5C, it is possible that K20R SUMOylation is required for additional SUMOylation events on other residues. One way to determine if Bonus is SUMOylated on multiple sites is to add recombinant SUMO protease to the extract and see if multiple higher molecular weight bands collapse into a single migrating species (implying multiple SUMOs) or multiple migrating species (implying something else is altering gel migration).

We appreciate the suggestion made by the reviewer. While we acknowledge the presence of occasional multiple bands in SUMO Western blots, the predominant pattern is the presence of unmodified Bon and a single additional band corresponding to SUMO-modified Bon. To investigate the possibility of multi-site SUMOylation, we performed requested experiment where we added SENP2 SUMO protease to the extract and checked Bon's SUMOylation. In the presence of NEM, we observed the unmodified form of Bon, as well as a single additional band representing a SUMO-modified form of Bon. Following SENP2 SUMO protease treatment, SUMOylation form of Bon was completely abolished in all samples, leaving only the unmodified Bon band (Extended Data Fig. 4D). This indicates that Bon is not SUMOylated on multiple sites and that the observed differential migration species likely result from other factors affecting gel migration.

3) The authors state that most upregulated genes in BonusGLKD are not highly enriched in H3K9me3. The heatmap in figure 3D is not an ideal presentation of this argument. The authors should show an example of what the signal on a highly enriched gene looks like for comparison. The authors also argue that because most upregulated genes in BonusGLKD are not highly enriched in H3K9me3, they must be indirectly repressed. Another possibility is that bonus-mediated H3K9me3 is only important (and present) during early nurse cell differentiation and is later lost and dispensable during the rapid endocycles. After bonus establishes repression though H3K9me3, it might be maintained through bonus-Mi2/Nurd, something else, or nothing at all. The authors could discuss this possibility or perform H3K9me3 ChIP during cyst formation and early nurse cell differentiation rather than in whole ovaries, which are enriched for later stages.

We thank the reviewer for their thoughtful comments and suggestions. In our revised manuscript we have included the tracks of gene that is highly enriched in H3K9me3 but remain unchanged upon Bon GLKD (Extended Data Fig. 3B). This addition allows for a visual comparison and better supports our argument that majority of genes upregulated in Bon GLKD are not enriched in H3K9me3 mark. We also appreciate the reviewer's suggestion regarding the potential temporal dynamics of Bon-mediated H3K9me3. It is indeed possible that Bon's role in establishing H3K9me3 might be more prominent during early nurse cell differentiation and less critical in later stages. We included discussion of this possibility in revised manuscript. To further explore it would be valuable to perform H3K9me3 ChIP during cyst formation and early nurse cell differentiation. However, given the limitations of our current resources and time limitations, we were unable to perform these experiments for the revised manuscript.

4) The BonusGLKD RNAseq analysis is underwhelming. The conclusion that "Bonus represses tissue-specific genes" has limited value. Every gene that is not expressed in ovaries is "tissue-specific." What subset of tissue-specific genes does Bonus repress? What common features do these genes have and how do they compare to other sets of tissue-specific genes, such as those reportedly repressed by setdb1, Polycomb proteins, small ovary, l(3)mbt, and stonewall (among others in female germ cells). Comparing these available data sets could help the authors understand the mechanism of Bonus repression and how BonusGLKD leads to sterility. The authors could also further analyze the differences between nos-Gal4 and MT-Gal4 to better understand why nos- but not MT-driven knockdown is sterile.

We appreciate the reviewer's feedback regarding the RNA-seq analysis and acknowledge the importance of identifying the specific subset of tissue-specific genes. The Figure 2C shows specific tissues where genes derepressed upon Bon GLKD are normally expressed. These are tissues/organs such as the head, digestive system, and nervous system. The reviewer's suggestion to compare our findings with existing datasets are valid and could indeed provide a more comprehensive understanding of Bon repression and its implications in female germ cells. However, many of the published datasets are based on mutant fly lines or use different GAL4 drivers to induce knockdowns, making direct comparisons challenging. We have conducted a preliminary analysis of available data, specifically nos-Gal4>SetDB1KD (GSE109852), and identified an overlap of 135 genes out of the 464 genes upregulated upon nos-Gal4>BonusKD with those affected by SetDB1 knockdown. We have included this result in the revised manuscript.

Main Study Limitations:

1) It is unclear which genes are directly vs indirectly regulated by bonus, which makes it difficult to understand Bonus's repressive mechanism. Several lines of experiments could help resolve this issue. 1) Bonus ChIPseq, which the authors mentioned was difficult. 2) RNAseq of BonusGLKD rescued with KR3 mutation. This would help separate SUMO/setdb1-dependent regulation from Mi-2 dependent regulation. Similarly, comparing differentially expressed genes in Su(var)2-10GLKD, setdb1GLKD, 3KR rescue, and MI-2 GLKD could identify overlapping targets and help refine how bonus represses subsets of genes through these different corepressors.

We appreciate the reviewer's suggestions and agree that discrimination between direct and indirect Bon targets should be the next step in understanding Bon repressive mechanism. We have previously attempted to determine Bon direct targets using ChIP-seq approach. However, despite our multiple efforts using both native Bon antibodies and GFP-tagged Bon fly lines, analysis of ChIP-seq data did not reveal specific enrichment indicating that Bon – similar to many other chromatin-bound proteins – are not amenable to ChIP. The recommendation for RNA-seq analysis of Bon GLKD rescued with the 3KR mutation is valuable, and we will certainly consider it for future investigations.

We compared differentially expressed genes in Su(var)2-10 GLKD and Mi-2 GLKD and found limited overlap: out of the 231 genes affected by Bon GLKD, 39 genes were affected in Mi-2 GLKD and 42 in Su(var)2-10 GLKD. We acknowledge the importance of understanding which genes are directly or indirectly regulated by Bon and the potential for further experiments to address this question.

2) The paper falls short in discussing how SUMO might promote repression. This is important when considering the conservation (of lack thereof) of SUMOylation sites in Tif1 proteins in distantly related animals. One piece of data that was not discussed is the apparent localization of SUMOylated bonus in the cytoplasmic fraction of the blot in Figure 5F. Su(var)2-10 is mostly a nuclear protein, so is bonus SUMOylated in the nucleus and then exported to the cytoplasm? Also, setdb1 is a nuclear protein, so it is unlikely that the SUMOylated bonus directly interacts with setdb1 on target genes. Together with Fig 5E (unSUMOylatable Bonus aggregates in the nucleus), one could make a model where SUMO solubilizes bonus (perhaps by disassembling aggregates) and indirectly allows it to associate with setdb1 and chromatin. It is also important to note that in Figure 5I, the K3R mutation appears to lessen but not eliminate Bonus interaction with setdb1. This data again disfavors a model where SUMO establishes an interaction interface between setdb1 and Bonus. To determine which form of Bonus interacts with setdb1, the authors could perform a setdb1 pulldown and monitor the SUMOylation state of coIPed Bonus through mobility shift. If mostly unSUMOylated bonus interacts with setdb1, and SUMO indirectly promotes Bonus interaction with setdb1 (perhaps by disassembling Bonus aggregates), then the precise locations of Bonus SUMOylation sites could more easily shift during evolution, disfavoring the author's convergent evolution hypothesis.

We appreciate the reviewer's valuable feedback. Regarding the observation of SUMOylated Bon in the cytoplasmic fraction in Figure 5F, we recognize its significance. This finding has prompted us to consider a model in which SUMOylation may play a role in translocating Bon from the nucleus to the cytoplasm, potentially influencing interactions with SetDB1 and chromatin indirectly. Furthermore, Figure 5I which shows only a partial reduction in Bon-SetDB1 interaction with the 3KR mutation, suggests that SUMO may not be the primary mediator of this interaction. We recognize the need for further investigations to clarify SUMO's exact role in this context. In response to the reviewer's suggestion, we conducted SetDB1 pulldown experiments in S2 cells. The results reveal that indeed SetDB1 primarily interacts with unmodified Bon which is by far more abundant compared to SUMOylated form (Extended Data Fig. 5C). We think this experiment presents certain technical challenges, as the signal for Bon, when used as prey in co-IP experiments, is relatively faint, making it inherently difficult to detect the lower levels of SUMO-modified Bon. Additionally, in revised manuscript we have added new result of determining Bon interactors in ovary using mass-spec analysis, which showed that SetDB1 associates with wild-type, but not SUMO-deficient Bon. While our data support the idea that SUMO may contribute to Bon solubilization, possibly by disassembling aggregates, thereby indirectly facilitating its association with SetDB1 and chromatin, we acknowledge that the precise mechanism remains unclear.

Reviewer #2 (Public Review):

Summary:

The authors analyze the functions and regulation of Bon, the sole Drosophila ortholog of the TIF1 family of mammalian transcriptional regulators. Bon has been implicated in several developmental programs; however, the molecular details of its regulation have not been well understood. Here, the authors reveal the requirement of Bon in oogenesis, thus establishing a previously unknown biological function for this protein. Furthermore, careful molecular analysis convincingly established the role of Bon in transcriptional repression. This repressor function requires interactions with the NuRD complex and histone methyltransferase SetDB1, as well as sumoylation of Bon by the E3 SUMO ligase Su(var)2-10. Overall, this work represents a significant advance in our understanding of the functions and regulation of Bon and, more generally, the TIF1 family. Since Bon is the only TIF1 family member in Drosophila, the regulatory mechanisms delineated in this study may represent the prototypical and important modes of regulation of this protein family. The presented data are rigorous and convincing. As discussed below, this study can be strengthened by a demonstration of a direct association of Bon with its target genes, and by analysis of the biological consequences of the K20R mutation.

Strengths:

1. This study identified the requirement for Bon in oogenesis, a previously unknown function for this protein.
2. Identified Bon target genes that are normally repressed in the ovary, and showed that the repression mechanism involves the repressive histone modification mark H3K9me3 deposition on at least some targets.
3. Showed that Bon physically interacts with the components of the NuRD complex and SetDB1. These protein complexes are likely mediating Bon-dependent repression.
4. Identified Bon sumoylation site (K20) that is conserved in insects. This site is required for repression in a tethering transcriptional reporter assay, and SUMO itself is required for repression and interaction with SetDB1. Interestingly, the K20-mutant Bon is mislocalized in the nucleus in distinct puncta.
5. Showed that Su(var)2-10 is a SUMO E3 ligase for Bon and that Su(var)2-10 is required for Bon-mediated repression.

Weaknesses:

The study would be strengthened by demonstrating a direct recruitment of Bon to the target genes identified by RNA-seq. Given that the global ChIP-seq was not successful, a few possibilities could be explored. First, Bon ChIP-qPCR could be performed on the individual targets that were functionally confirmed (e.g. rbp6, pst). Second, a global Bon ChIP-seq has been reported in PMID: 21430782 - these data could be used to see if Bon is associated with specific targets identified in this study. In addition, it would be interesting to see if there is any overlap with the repressed target genes identified in Bon overexpression conditions in PMID: 36868234.

We greatly appreciate the reviewer's suggestion to demonstrate the direct recruitment of Bon to the target genes. As described in our answer to reviewer #1, we attempted to determine Bon direct targets using ChIP-seq approach using both native Bon antibodies and GFP-tagged Bon fly lines. However, analysis of ChIP-seq data did not reveal specific enrichment. Similarly, Bon ChIP-qPCR on individual targets showed the same results suggesting that Bon – similar to many other chromatin-bound proteins – are not amenable to ChIP protocol, at least in standard conditions. To further explore this issue, we have analyzed results of a global Bon ChIP-seq reported in PMID: 21430782. We did not find Bon binding to individual targets, but even more importantly, we did not see clear Bon enrichment elsewhere in the genome confirming a conclusion that Bon targets on chromatin cannot be determined by ChIP. Additionally, we explored the possibility of overlap between target genes repressed by Bon in our study and those observed under Bon overexpression conditions in PMID: 36868234. While we did identify 41 genes in common, it's important to note that the datasets are derived from different tissues (pupal eyes vs. ovaries), making direct comparison problematic.

The second area where the manuscript can be improved is to analyze the biological function of the K20R mutant Bonus protein. The molecular data suggest that this residue is important for function, and it would be important to confirm this in vivo.

We appreciate the reviewer's suggestion to analyze the biological function of the K20R mutant Bon protein. While we acknowledge that we did not use single-site K20R mutant for in vivo experiments, we demonstrated that the mutant with the three-residue substitution (3KR) is incapable of inducing repression (Figure 5G). Given that other experiments consistently showed that K20 is the primarily SUMOylation site, this result supports the conclusion that K20 SUMOylation plays an important role in Bon-mediated transcriptional silencing.

Reviewer #1 (Recommendations for The Authors):

Make the RNAseq and ChIPseq data publicly available!

The sequencing data have been deposited to the NCBI GEO archive. The accession number for all other RNA-seq and ChIP-seq data reported in this paper is GEO: GSE241375.

Reviewer #2 (Recommendations for The Authors):

It would be interesting to identify the biological basis of aberrant ovary development in Bon depletion conditions. Previous studies (e.g. PMID: 11336699) suggested that Bon loss of function clones are cell lethal, and the developmental defects in oogenesis presented in the current study offer an opportunity to delve more into the causes of cell loss, e.g. by showing that the cells die via apoptosis.

Thank you for your valuable suggestion. In response to your comment, we performed a TUNEL assay to investigate whether germ cells in nos-Gal4>BonusKD ovaries undergo apoptosis. Our results indeed indicate that germ cells in these ovaries exhibit apoptosis, as evidenced by the TUNEL signal (Extended Data Fig. 1C). This information has been included in the revised manuscript to provide insights into the biological basis of aberrant ovary development in Bon depletion conditions.

The K20 residue could also be ubiquitinated. This possibility could at least be discussed, particularly given the presence of the RING Ub ligase domain in Bon that might potentially perform self-ubiquitination.

Indeed, the possibility that Bon can be ubiquitinated is a valid consideration. We have explored this possibility. We did not detect any signals with the Ubiquitin antibody in both wild-type Bon immunoprecipitant and triple-mutant [3KR] ovaries (in which K20 is also mutated) (Extended Data Fig. 4C). This suggests that K20 is more likely responsible for Bon SUMOylation rather than ubiquitination. We appreciate the reviewer's suggestion and have included this information into the revised manuscript.

Note: This response was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Dear Editor,

Herewith we submit our fully revised peer-reviewed preprint that had been reviewed by Review Commons. We thank the Review Commons team and reviewers for thoroughly commenting on our preprint and providing very useful additional points for consideration and discussion.

You will find - the revised manuscript (third preprint version uploaded on biorxiv)<br /> - two reviewer letters (through Review Commons), - our rebuttal letter<br /> - a revised manuscript version with highlighted changes.

Our manuscript reports that an active form of FIT, an essential transcription factor for root iron acquisition in plants, forms dynamic nuclear condensates in response to a blue light stimulus.<br /> A hallmark of our work is the thorough investigation of the nature of the FIT nuclear bodies in plant cells, that we were able to characterize as highly dynamic condensates in which active FIT homo- and heteromeric protein complexes can accumulate preferentially. Through co-localization with nuclear body markers, we found that these FIT condensates are related to speckles, which are a sub-type of nuclear bodies connected with splicing activities. This suggests that FIT condensates are linked with post-transcriptional regulation mechanisms.

The reviewers highlight that an “impressive set of microscopic techniques” has been combined to study in a unique manner the characteristics and functionalities of FIT nuclear bodies in living plant cells. We show that FIT nuclear bodies can be formed in roots of Arabidopsis thaliana. The microscopic imaging techniques we used to characterize the nature and functionalities of FIT nuclear bodies in plant cells have several constraints related to sensitivity and a required strength of fluorescent protein signal. For technical reasons to be able to apply qualitative and quantitative imaging techniques, we conducted the investigation of FIT condensates in Nicotiana benthamiana, a classical and widely used plant protein expression system.

As stated in the reviews, the connection between plant nutrition and nuclear bodies is an “unprecedented” new mode of regulation. The significance of our work is underlined by the fact that we report a “very precise cellular and molecular mechanism in nutrition” that is as yet “still largely unexplored in this context”. Therefore, our study “sheds light on the functional role of this membrane-less compartment and will be appreciated by a large audience.”

We propose that condensate formation is a mechanism that may steer iron nutrition responses by providing a link between iron and light signaling. For sessile plants, it is absolutely essential that environmental signals are sensed and integrated with developmental and physiological programs so that plants can rapidly adjust to a changing environment and potential stress situations. Since iron is a micronutrient that may be toxic when present in excess, e.g. through catalyzing oxidative stress, plants strictly control the acquisition and allocation of iron. Hence, FIT nuclear bodies may be regulatory hubs that integrate at the sub-nuclear level environmental signaling inputs in the control of micronutrient uptake, possibly connected with splicing.

Our work lays the ground for future studies that can address the proof of concept in more detailed manner in plants exposed to varying environmental conditions to reveal the interconnection of environmental and nutritional signaling.

We prepared a revised preprint in which we address all reviewer comments. Please find our revision and our detailed response to all reviewer comments.

With these changes, we hope that our peer-reviewed preprint can receive a positive vote,

We are looking forward to your response,

Sincerely

Petra Bauer and Ksenia Trofimov on behalf of all authors

Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

In this paper entitled " FER-LIKE IRON DEFICIENCY-INDUCED TRANSCRIPTION FACTOR (FIT) accumulates in homo- and heterodimeric complexes in dynamic and inducible nuclear condensates associated with speckle components", Trofimov and colleagues describe for the first time the function of FIT in nuclear bodies. By an impressive set of microscopies technics they assess FIT localization in nuclear bodies and its dynamics. Finally, they reveal their importance in controlling iron deficiency pathway. The manuscript is well written and fully understandable. Nonetheless, at it stands the manuscript present some weakness by the lack of quantification for co-localization and absence controls making hard to follow authors claim. Moreover, to substantially improve the manuscript the authors need to provide more proof of concepts in A. thaliana as all the nice molecular and cellular mechanism is only provided in N. bentamiana. Finally, some key conclusions in the paper are not fully supported by the data.<br /> Please see below:

Main comments:

1) For colocalization analysis, the author should provide semi-quantitative data counting the number of times by eyes they observed no, partial or full co-localization and indicate on how many nucleus they used.

Authors:

We have added the information in the Materials and Method section, lines 731-734:

In total, 3-4 differently aged leaves of 2 plants were infiltrated and used for imaging. One infiltrated leaf with homogenous presence of one or two fluorescence proteins was selected, depending on the aim of the experiment, and ca. 30 cells were observed. Images are taken from 3-4 cells, one representative image is shown.

In all analyzed cases, except in the case of colocalization of FIT and PIF4 fusion proteins, the ca. 30 cells had the same localization and/or colocalization patterns. This information has also been added in the figure legends. Each experiment was repeated at least 2-3 times, or as indicated in the figure legend.

2) Do semi-quantitative co-localization analysis by eyes, on FIT NB with known NB makers in the A. thaliana root. For now, all the nicely described molecular mechanism is shown in N. benthamiana which makes this story a bit weak since all the iron transcriptional machinery is localized in the root to activate IRT1.

Authors:

The described approach has been very optimal, and we were able to screen co-localizing marker proteins in FIT NBs in N. benthamiana to better identify the nature of FIT NBs. This has been successful as we were able to associate FIT NBs with speckles. The N. benthamiana system allowed optimal microscopic observation of fluorescence proteins and quantification of FIT NB characteristics in contrast to the root hair zone of Arabidopsis where Fe uptake takes place. FIT is expressed at a low level in roots and also in leaves, whereby fluorescence protein expression levels are insufficient for the here-presented microscopic studies. The tobacco infiltration system is also well established to study FIT-bHLH039 protein interaction and nuclear body markers. We discuss this point in the discussion, see line 489-500.

3) The authors need to provide data clearly showing that the blue light induce NB in A. thaliana and N. benthamiana.

Authors:

For tobacco, see Figure 1B (t = 0, 5 min) and Supplemental Movies S1. For Arabidopsis, please see Figure 1A (t = 0, 90 and 120 min) and Supplemental Figure S1A. We provide an additional image of pFIT:cFIT-GFP Arabidopsis control plants, showing that NB formation is not detected in plants that were grown in white light and not exposed to blue light before inspection (Supplemental Figure S1B). We state, that upon blue light exposure, plants had FIT NBs in at least 3-10 nuclei of 20 examined nuclei in the root epidermis in the root hair zone (in three independent experiments with three independent plants). White-light-treated plants showed no NB formation unless an additional exposure to blue light was provided (in three independent experiments, three independent plants per experiment and with 15 examined nuclei per plant).

4) Direct conclusion in the manuscript:

• Line 170: At this point of the paper the author cannot claim that the formation of FIT condensates in the nucleus is due to the light as it might be indirectly linked to cell death induced by photodamaging the cell using a 488 lasers for several minutes. This is true especially with the ELYRA PS which has strong lasers made for super resolution and that Cell death is now liked to iron homeostasis. The same experiment might be done using a spinning disc or if the authors present the data of the blue light experiment mentioned above this assumption might be discarded. Alternatively, the author can use PI staining to assess cell viability after several minutes under 488nm laser.

Authors:

As stated in our response to comment 3, we have included now a white light control to show that FIT NB formation is not occurring under the normal white light conditions. Since the formation of FIT NBs is a dynamic and reversible process (Figure 1A), it indicates that the cells are still viable, and that cell death is not the reason for FIT NB formation.

• Line 273: I don't agree with the first part of the authors conclusion, saying that "wild-type FIT had better capacities to localize to NBs than mutant FITmSS271AA, presumably due its IDRSer271/272 at the C-terminus. This is not supported by the data. In order to make such a claim the author need to compare the FA of FIT WT with FITmSS271AA by statistical analysis. Nonetheless, the value seems to be identical on the graphs. The main differences that I observed here are, 1) NP value for FITmSS271AA seems to be lower compared to FIT-WT, suggesting that the Serine might be important to regulate protein homedimerization partitioning between the NP and the NB. 2) To me, something very interesting that the author did not mention is the way the FA of FITmSS271AA in the NB and NP is behaving with high variability. The FA of those is widely spread ranging from 0.30 to 0.13 compared to the FIT-WT. To me it seems that according to the results that the Serine 271/272 are required to stabilize FIT homodimerization. This would not only explain the delay to form the condensate but also the decreased number and size observed for FITmSS271AA compared to FIT-WT. As the homodimerization occurs with high variability in FITmSS271AA, there is less chance that the protein will meet therefore decreasing the time to homodimerize and form/aggregate NB.

Authors:

We fully agree. We meant to describe this result it in a similar way and thank you for help in formulating this point even better. Rephrasing might make it better clear that the IDRSer271/272 is important for a proper NB localization, lines 272-278:

“Also, the FA values did not differ between NBs and NP for the mutant protein and did not show a clear separation in homodimerizing/non-dimerizing regions (Figure 3D) as seen for FIT-GFP (Figure 3C). Both NB and NP regions showed that homodimers occurred very variably in FITmSS271AA-GFP.

In summary, wild-type FIT could be partitioned properly between NBs and NP compared to FITmSS271AA mutant and rather form homodimers, presumably due its IDRSer271/272 at the C-terminus.”

• Line 301: According to my previous comment (line 273), here it seems that the Serine 271/272 are required only for proper partitioning of the heterodimer FIT/BHLH039 between the NP and NB but not for the stability of the heterodimer formation. However, it might be great if the author would count the number of BHLH039 condensates in both version FITmSS271AA and FIT-WT. To my opinion, they would observe less BHLH039 condensate because the homodimer of FITmSS271AA is less likely to occur because of instability.

Authors:

bHLH039 alone localizes primarily to the cytoplasm and not the nucleus, and the presence of FIT is crucial for bHLH039 nuclear localization (Trofimov et al., 2019). Moreover, bHLH039 interaction with FIT depends on SS271AA (Gratz et al., 2019). We therefore did not consider this experiment for the manuscript and did not acquire such data, as we did not expect to achieve major new information.

5) To wrap up the story about the requirements of NB in mediating iron acquisition under different light regimes, provide data for IRT1/FRO2 expression levels in fit background complemented with FITmSS271AA plants. I know that this experiment is particularly lengthy, but it would provide much more to this nice story.

Authors:

Data for expression of IRT1 and FRO2 in FITmSS271AA/fit-3 transgenic Arabidopsis plants are provided in Gratz et al. (2019). To address the comment, we did here a NEW experiment. We provide gene expression data on FIT, BHLH039, IRT1 and FRO2 splicing variants (previously reported intron retention) to explore the possibility of differential splicing alterations under blue light (NEW Supplemental Figure S6 and S7, lines 454-466). Very interestingly, this experiment confirms that blue light affects gene expression differently from white light in the short-term NB-inducing condition and that blue light can enhance the expression of Fe deficiency genes despite of the short 1.5 to 2 h treatment. Another interesting aspect was that the published intron retention was also detected. A significant difference in intron retention depending on iron supply versus deficiency and blue/white light was not observed, as the pattern of expression of transcripts with respective intron retentions sites was the same as the one of total transcripts mostly spliced.

Minor comments

In general, I would suggest the author to avoid abbreviation, it gets really confusing especially with small abbreviation as NB, NP, PB, FA.

Authors:

We would like to keep the used abbreviations as they are utilized very often in our work and, in our eyes, facilitate the understanding.

Line 106: What does IDR mean?

Authors:

Explanation of the abbreviation was added to the text, lines 105-108:

“Intrinsically disordered regions (IDRs) are flexible protein regions that allow conformational changes, and thus various interactions, leading to the required multivalency of a protein for condensate formation (Tarczewska and Greb-Markiewicz, 2019; Emenecker et al., 2020).”

Line 163-164: provide data or cite a figure properly for blue light induction.

Authors:

We have removed this statement from the description, as we provide a white light control now, lines 157-158:

“When whole seedlings were exposed to 488 nm laser light for several minutes, FIT became re-localized at the subnuclear level.”

Line 188: Provide Figure ref.

Authors:

Figure reference was added to the text, lines 184-185:

“As in Arabidopsis, FIT-GFP localized initially in uniform manner to the entire nucleus (t=0) of N. benthamiana leaf epidermis cells (Figure 1B).”

Line 194: the conclusion is too strong. The authors conclude that the condensate they observed are NB based on the fact the same procedure to induce NB has been used in other study which is not convincing. Co-localization analysis with NB markers need to be done to support such a claim. At this step of the study, the author may want to talk about condensate in the nucleus which might correspond to NB. Please do so for the following paragraph in the manuscript until colocalization analysis has not been provided. Alternatively provide the co-localization analysis at this step in the paper.

Authors:

We agree. We changed the text in two positions.

Lines 176-178__: “__Since we had previously established a reliable plant cell assay for studying FIT functionality, we adapted it to study the characteristics of the prospective FIT NBs (Gratz et al., 2019, 2020; Trofimov et al., 2019).”

Lines 192-193: “__We deduced that the spots of FIT-GFP signal were indeed very likely NBs (for this reason hereafter termed FIT NBs).”

Line 214: In order to assess the photo bleaching due to the FRAP experiment the quantification of the "recovery" needs to be provided in an unbleached area. This might explain why FIT recover up to 80% in the condensate. Moreover, the author conclude that the recovery is high however it's tricky to assess since no comparison is made with a negative/positive control.

Authors:

In the FRAP analysis, an unbleached area is taken into account and used for normalization.

We reformulated the description of Figure 1F, lines 212-214:

“According to relative fluorescence intensity the fluorescence signal recovered rapidly within FIT NBs (Figure 1F), and the calculated mobile fraction of the NB protein was on average 80% (Figure 1G).”

Line 220-227: The conclusion it's too strong as I mentioned previously the author cannot claim that the condensate are NBs at this step of the study. They observed nuclear condensates that behave like NB when looking at the way to induce them, their shape, and the recovery. And please include a control.

Authors:

Please see the reformulated sentences and our response above.

Lines 176-178: “Since we had previously established a reliable plant cell assay for studying FIT functionality, we adapted it to study the characteristics of the prospective FIT NBs (Gratz et al., 2019, 2020; Trofimov et al., 2019).”

Lines 192-193: “__We deduced that the spots of FIT-GFP signal were indeed very likely NBs (for this reason hereafter termed FIT NBs).”

Line 239: It's unappropriated to give the conclusion before the evidence.

Authors:

Thank you. We removed the conclusion.

Line 240: Figure 2A, provide images of FIT-G at 15min in order to compare. And the quantification needs to be provided at 5 minutes and 15 minutes for both FIT-G WT and FIT-mSS271AA-G counting the number of condensates in the nucleus. Especially because the rest of the study is depending on these time points.

Authors:

This information is provided in the Supplemental Movie S1C.

Line 241: the author say that the formation of condensate starts after 5 minutes (line 190) here (line 241) the author claim that it starts after 1 minutes. Please clarify.

Authors:

In line 190 we described that FIT NB formation occurs after the excitation and is fully visible after 5 min. In line 241 we stated that the formation starts in the first minutes after excitation, which describes the same time frame. We rephrased the respective sentences.

Lines 185-188: “A short duration of 1 min 488 nm laser light excitation induced the formation of FIT-GFP signals in discrete spots inside the nucleus, which became fully visible after only five minutes (t=5; Figure 1B and Supplemental Movie S1A).”

Lines 239-242: “While FIT-GFP NB formation started in the first minutes after excitation and was fully present after 5 min (Supplemental Movie S1A), FITmSS271AA-GFP NB formation occurred earliest 10 min after excitation and was fully visible after 15 min (Supplemental Movie S1C).”

Line 254: Not sure what the authors claim "not only for interaction but also for FIT NB formation ". To me, the IDR is predicted to be perturbed by modeling when the serines are mutated therefore the IDR might be important to form condensates in the nucleus. Please clarify.

Authors:

The formation of nuclear bodies is slow for FITmSS271AA as seen in Figure 2. Previously, we showed that FITmSS271AA homodimerizes less (Gratz et al., 2019.) Therefore, the said IDR is important for both processes, NB formation and homodimerization. We have added this information to make the point clear, lines 253-255:

“This underlined the significance of the Ser271/272 site, not only for interaction (Gratz et al., 2019) but also for FIT NB formation (Figure 2).”

Line 255: It's not clear why the author test if the FIT homodimerization is preferentially associated with condensate in the nucleus.

Authors:

We test this because both homo- and heterodimerization of bHLH TFs are generally important for the activity of TFs, and we unraveled the connection between protein interaction and NB formation. We state this in lines 228-232.

Line 269-272: It's not clear to what the authors are referring to.

Authors:

We are describing the homodimeric behavior of FIT and FITmSS271AA assessed by homo-FRET measurements that are introduced in the previous paragraph, lines 256-268.

Line 309: This colocalization part should be presented before line 194.

Authors:

We find it convincing to first examine and characterize the process underlying FIT NB formation, then studying a possible function of NBs. The colocalization analysis is part of a functional analysis of NBs. We thank the reviewer for the hint that colocalization also confirms that indeed the nuclear FIT spots are NBs. We will take this point and discuss it, lines 516-522:

“Additionally, the partial and full colocalization of FIT NBs with various previously reported NB markers confirm that FIT indeed accumulates in and forms NBs. Since several of NB body markers are also behaving in a dynamic manner, this corroborates the formation of dynamic FIT NBs affected by environmental signals.”

“In conclusion, the properties of liquid condensation and colocalization with NB markers, along with the findings that it occurred irrespective of the fluorescence protein tag preferentially with wild-type FIT, allowed us to coin the term of ‘FIT NBs’.”

Line 328: add the ref to figure, please.

Authors:

Figure reference was added to the text, lines 330-332:

“The second type (type II) of NB markers were partially colocalized with FIT-GFP. This included the speckle components ARGININE/SERINE-RICH45-mRFP (SR45) and the serine/arginine-rich matrix protein SRm102-mRFP (Figure 5).”

Line 334: It seems that the size of the SR45 has an anormal very large diameter between 4 and 6 µm. In general a speckle measure about 2-3µm in diameter. Can the author make sure that this structure is not due to overexpression in N. benthamiana or make sure to not oversaturate the image.

Authors:

Thank you for this hint. Indeed, there are reports that SR45 is a dynamic component inside cells. It can redistribute depending on environmental conditions and associate into larger speckles depending on the nuclear activity status (Ali et al., 2003). We include this reference and refer to it in the discussion, lines 557-564:

“Interestingly, typical FIT NB formation did not occur in the presence of PB markers, indicating that they must have had a strong effect on recruiting FIT. This is interesting because the partially colocalizing SR45, PIF3 and PIF4 are also dynamic NB components. Active transcription processes and environmental stimuli affect the sizes and numbers of SR45 speckles and PB (Ali et al., 2003; Legris et al., 2016; Meyer, 2020). This may indicate that, similarly, environmental signals might have affected the colocalization with FIT and resulting NB structures in our experiments. Another factor of interference might also be the level of expression.”

Line 335: It seems that the colocalization is partial only partial after induction of NB. The FIT NB colocalize around SR45. But it's hard to tell because the images are saturated therefore creating some false overlapping region.

Authors:

The localization of FIT with SR45 is partial and occurs only after FIT has undergone condensation, see lines 335-338.

Line 344-345: It's unappropriated to give the conclusion before the evidence.

Authors:

We explain at an earlier paragraph that we will show three different types of colocalization and introduce the respective colocalization types within separate paragraphs accordingly, see lines 314-321.

Line 353: increase the contrast in the image of t=5 for UAP56H2 since it's hard to assess the colocalization.

Authors:

This is done as noted in the figure legend of Figure 6.

Line 381-382: "In general" does not sound scientific avoid this kind of wording and describe precisely your findings.

Authors:

We rephrased the sentence, line 387-388:

Localization of single expressed PIF3-mCherry remained unchanged at t=0 and t=15 (Supplemental Figure S5A).

Line 384-385: Provide the data and the reference to the figure.

Authors:

We apologize for the misunderstanding and rephrased the sentence, line 389-391:

After 488 nm excitation, FIT-GFP accumulated and finally colocalized with the large PIF3-mCherry PB at t=15, while the typical FIT NBs did not appear (Figure 7A)

Line 386: The structure in which FIT-G is present in the Figure 7A t=15 is not alike the once already observed along the paper. This could be explained by over-expression in N. benthamiana. Please explain.

Authors:

Thank you for the hint. We discuss this in the discussion part, see lines 555-568.

Line 393: Explain and provide data why the morphology of PIF4/FIT NB do not correspond to the normal morphology.

Authors:

Thank you for the valuable hints. Several reasons may account for this and we provide explanations in the discussion, see lines 555-568.

Line 396-398: It seems also from the data that co-expression of PIF4 of PIF3 will affect the portioning of FIT between the NP and the NB.

Authors:

We can assume that residual nucleoplasm is depleted from protein during NB formation. This is likely true for all assessed colocalization experiments. We discuss this in lines 492-494.

The discussion is particularly lengthy it might be great to reduce the size and focus on the main findings.

Authors:

We shortened the discussion.

Referees cross-commenting

All good for me, I think that the comments/suggestions from Reviewer #2 are valid and fair. If they are addressed they will improve considerably the manuscript.

Reviewer #1 (Significance):

This manuscript is describing an unprecedent very precise cellular and molecular mechanism in nutrition throughout a large set of microscopies technics. Formation of nuclear bodies and their role are still largely unexplored in this context. Therefore, this study sheds light on the functional role of this membrane less compartment and will be appreciated by a large audience. However, the fine characterization is only made using transient expression in N. Bentamiana and only few proofs of concept are provided in A. thaliana stable line.

Reviewer #2 (Evidence, reproducibility and clarity):

The manuscript of Trofimov et al shows that FIT undergoes light-induced, reversible condensation and localizes to nuclear bodies (NBs), likely via liquid-liquid phase separation and light conditions plays important role in activity of FIT. Overall, manuscript is well written, authors have done a great job by doing many detailed and in-depth experiments to support their findings and conclusions.

However, I have a number of questions/comments regarding the data presented and there are still some issues that authors should take into account.

Major points/comments:

1) Authors only focused on blue light conditions. Is there any specific reason for selecting only blue light and not others (red light or far red)?

Authors:

There are two main reasons: First, in a preliminary study (not shown) blue light resulted in the formation of the highest numbers of NBs. Second, iron reductase activity assays and gene expression analysis under different light conditions showed a promoting effect under blue light, but not red light or dark red light (Figure 9). This indicated to us, that blue light might activate FIT, and that active FIT may be related to FIT NBs.

2) Fig. 3C and D: as GFP and GFP-GFP constructs are used as a reference, why not taking the measurements for them at two different time points for example t=0 and t=5 0r t=15???

Authors:

Free GFP and GFP-GFP dimers are standard controls for homo-FRET that serve to delimit the range for the measurements.

3) Line 27-271: Acc to the figure 3d, for the Fluorescence anisotropy measurement of NBs appears to be less. Please explain.

Authors:

FA in NBs with FITmSS271AA is variable and the value is lower than that of whole nucleus but not significantly different compared with that in nucleoplasm. We describe the results of Figure 3D in lines 272-275.

4) Figure 4: For the negative controls, data is shown at only t=0, data should be shown at t=5 also to prove that there is no decrease in fluorescence in these negative controls when they are expressed alone without bhlh39 as there is no acceptor in this case.

Authors:

Neither for FIT/bHLH039 nor the FITmSS271AA/bHLH039 pair, there is a significant decrease in the fluorescence lifetime values between t=0 and t=5/15. FIT-G is a control to delimit the range. The interesting experiment is to compare the protein pairs of interest between the different nuclear locations at t=5/15.

5) Line 300-301: In Figure 4D and 4E. Fluorescence lifetime of G measurement at t=0 seems very similar for both FIT-G as well as FITmSS but if we look at the values of t=0 for FIT-G+bhlh039 it is greater than 2.5 and for FITmSS271AA-G+bhlh039 it is less which suggests more heterodimeric complexes to be formed in FITmSS271AA-G+bhlh039. Similar pattern is observed for NBs and NPs, according to the figure 4d and E.

Therefore, heterodimeric complexes accumulated more in case of FITmSS271AA-G+bhlh039 as compared to FIT-G+bhlh039 (if we compare measurement values of Fluorescence lifetime of G of FITmSS271AA-G+bhlh039 with FIT-G+bhlh039).

Please comment and elaborate about this further.

Authors:

These conclusions are not valid as the experiments cannot be conducted in parallel. Since the experiments had to be performed on different days due to the duration of measurements including new calibrations of the system, we cannot compare the absolute fluorescence lifetimes between the two sets.

6) Figure 4: For the negative controls, data is shown at only t=0, data should be shown at t=5 also to prove that there is no decrease in fluorescence in these negative controls when they are expressed alone without bhlh39 as there is no acceptor in this case.

Authors:

Please see our response to your comment 4).

7) Line 439-400: As iron uptake genes (FRO2 and IRT1) are more induced in WT under blue light conditions and FRO2 is less induced in case of red-light conditions. So, what happens to Fe content of WT grown under blue light or red light as compared to WT grown under white light. Perls/PerlsDAb staining of WT roots under different light conditions will add more information to this.

Authors:

We focused on the relatively short-term effects of blue light on signaling of nuclear events that could be related to FIT activity directly, particularly gene expression and iron reductase activity as consequence of FRO2 expression. These are both rapid changes that occur in the roots and can be measured. We suspect that iron re-localization and Fe uptake also occur, however, in our experience differences in metal contents will not be directly significant when applying the standard methods like ICP-MS or PERLs staining.

Minor comments:

Line 75-76: Rephrase the sentence

Authors:

We rephrased the sentence, lines 73-74:

“As sessile organisms, plants adjust to an ever-changing environment and acclimate rapidly. They also control the amount of micronutrients they take up.”

Line 119: Rephrase the sentence

Authors:

We rephrased the sentence, line 118-119:

“Various NBs are found. Plants and animals share several of them, e.g. the nucleolus, Cajal bodies, and speckles.”

Line 235-236: rephrase the sentence

Authors:

We rephrased the sentence, line 232-234:

“In the work of Gratz et al. (2019), the hosphor-mimicking FITmS272E protein did not show significant changes in its behavior compared to wild-type FIT.”

Line 444: Correct the sentence “Fe deficiency versus sufficiency”

Authors:

We corrected that, line 449-451:

“In both, the far-red light and darkness situations, FIT was induced under iron deficiency versus sufficiency, while on the other side, BHLH039, FRO2 and IRT1 were not induced at all in these light conditions (Figure 9I-P).”

Referees cross-commenting

I agree with R1 suggestions/comments and i think manuscript quality will be much better if authors carry out the experiments suggested by R1. I believe this will also strengthen their conclusions.

Reviewer #2 (Significance):

Overall, manuscript is well written, authors have done a nice job by doing several key experiments to support their findings and conclusions. However, the results and manuscript can be improved further by addressing some question raised here. This study is interesting for basic scientists which unravels the crosstalk of light signaling in nutrient signaling pathways.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

1. EVIDENCE, REPRODUCIBILITY AND CLARITY

Summary:

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate). Please place your comments about significance in section 2.

This work examines the active compensation of TDH3 by its paralogs TDH1 and TDH2 as a mechanism of robustness against genetic perturbations in yeast. The authors demonstrate that the paralogs compensate in a dose-dependent manner in response to TDH3's absence, mediated by shared transcriptional regulators Gcr1p and Rap1p. Furthermore, other glycolytic genes regulated by Gcr1p and Rap1p show similar changes in expression, indicating that active compensation of TDH3 is part of a greater homeostatic feedback mechanism. Additionally, the authors suggest that the ability of paralogs to actively compensate for each other and contribute to genetic robustness is actively selected for or is simply a side effect of their ancestrally shared regulators with sensitivity to feedback mechanisms.

Major comments:

• Are the claims and the conclusions supported by the data or do they require additional experiments or analyses to support them?

The authors present robust evidence in this paper to substantiate their claims and conclusions. The comprehensive data provided effectively establishes a clear and compelling case for the role of active compensation among the TDH paralogs. I think that the authors' conclusions are well-supported with the data. Further experiments are not warranted at this time.

• Please request additional experiments only if they are essential for the conclusions. Alternatively, ask the authors to qualify their claims as preliminary or speculative, or to remove them altogether.

No need for further experiments to support the manuscript's conclusions at this time.

• If you have constructive further reaching suggestions that could significantly improve the study but would open new lines of investigations, please label them as "OPTIONAL".

Dear authors, I have a couple of experiments to open further lines of investigation:

Considering the modest expression level increase resulting from gene duplication of TDH3 (~35%), it may be worthwhile to further explore this phenomenon and its potential relationship with the limited availability of GRC1 and RAP1 transcription factors. It is conceivable that an attenuation mechanism could be involved in regulating TDH3 expression, and an examination of this possibility would provide valuable insights. An experimental approach utilizing a titratable promoter and assessment of mRNA and protein levels would offer a compelling means to probe this inquiry. (OPTIONAL).

The strain expressing TDH3 at 135% of the wild-type expression level carries two copies of TDH3, but both copies have mutations in their promoter that reduce their individual expression relative to the wild-type alleles. We have clarified the text by adding “reducing expression levels from each promoter” on page 6, line 17.

The authors' discussion raises the question of whether the active compensation observed between the TDH paralogs is a result of selection or simply a consequence of their shared regulators. To address this question, one potential avenue for future research would be to test the ability of TDH1-2 gene products to compensate for the loss of TDH3 by expressing them under the TDH3 promoter, a stronger or an inducible promoter, and then, measuring the fitness of the resulting strains with a tdh3𝚫 background. This additional line of experimentation has the potential to improve our understanding of the regulatory networks involved and shed light on the selective pressures that contribute to the maintenance of these paralogs over evolutionary time. (OPTIONAL)

We agree that this question - how selection has acted on the catalytic activity of the three paralogous proteins in concert with their expression levels - is very interesting. In fact, experiments including those described by the reviewer are currently underway in the Wittkopp lab and will be the focus of a future manuscript.

• Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated time investment for substantial experiments.

Not applicable.

• Are the data and the methods presented in such a way that they can be reproduced?

Yes.

• Are the experiments adequately replicated and statistical analysis adequate?

Yes.

Minor comments:

• Specific experimental issues that are easily addressable.

In the introduction of the manuscript (pp. 4 para. 1), it would be useful to provide a more comprehensive overview of the gene expression patterns and protein abundances of the three TDH paralogs. Including such information would better enable readers to understand the functional roles of these paralogs.

We have added a new figure (Figure S1) showing differences in expression levels and patterns across the growth curve for the three paralogs. In addition, we have added some discussion of the differences in the effects of trans-regulatory mutations on protein abundance of each paralog that was recently published by another group and further indicates some level of regulatory divergence, particularly for TDH1 (pp.4, lines 12-19).

It would be helpful to report the phenotype of the tdh1𝚫/tdh2𝚫 double mutant to provide a clearer understanding of the functional overlap of these paralogs.

The revised manuscript includes additional information about divergence in expression patterns and differences in the effects of trans-regulatory mutations between TDH1 and the other two paralogs. Specifically, TDH1 is expressed under different conditions, and it is likely involved in different processes, than TDH2 and TDH3 (pp.4, lines 12-19, Figure S1). We have also added a sentence to the introduction stating that the double mutant deleting TDH1 and TDH3 has the same growth rate as TDH3 mutants alone, suggesting that TDH1 does not compensate for loss of TDH3 in the same way that TDH2 does. Because of these observations and because of the stronger overlap in expression profiles of TDH2 and TDH3, we have chosen to focus primarily on the compensation for TDH3 by TDH2 in the revised manuscript. We believe that these changes make the TDH1/TDH2 double mutant phenotype (which has not been studied as closely as the double mutants of TDH1 or TDH2 with TDH3) unnecessary for this study.

In the results section (pp. 5, para. 2), while it is understandable that the authors have focused on the transcriptional regulation of these paralogs, it would also be insightful to provide data on their respective protein abundances, as posttranslational regulation is often a crucial component of gene expression. This data may already be available in other high-throughput studies.

We have added new experimental data using fluorescent fusion proteins that shows that the protein abundance of TDH2 increases in response to deletion of TDH3 (Figure 1B). The results of our fluorescence measurements correspond well with transcriptional levels indicated by RNA-seq, indicating that the upregulation of TDH2 expression we saw in TDH3 mutants was controlled primarily at the transcriptional level.

It would be valuable to include more detailed information on the shared cis-regulatory elements between these genes, as this could provide further insight into their regulation and potential functional divergence.

According to experimental data compiled in http://www.yeastract.com/ , ChIP-exo data indicates that promoters for TDH1, TDH2, and TDH3 are all directly bound by Gcr1p (and the complex partner Gcr2p), although the evidence for Gcr1p binding is weaker at TDH1 than the other two paralogs, and this study does not identify Gcr1p TFBS motifs in the promoters of either TDH1 or TDH2 (Holland et al. 2019). However, we were able to locate Gcr1p TFBS motifs (CTTCC, Baker 1991) in the TDH2 promoter by manually searching regions annotated as bound by Gcr1’s complex partner Gcr2p in another publicly available ChIP-chip dataset (MacIsaac et al. 2006). We mutated these four motifs in a copy of the TDH2 promoter driving YFP expression to test for their role in upregulation using flow cytometry. We found that mutation or deletion of these putative TFBS reduced the overall activity of the promoter, indicating that these sequences are functional, and also observed that upon mutation or deletion of these putative TFBSs reduced the upregulation of TDH2 when TDH3 was deleted (Figure 3E). A schematic of the TDH2 promoter has been added to Figure 3 describing these experiments.

• Are prior studies referenced appropriately?

Yes.

• Are the text and figures clear and accurate?

The language used in this manuscript is clear and concise, making the material easily comprehensible to readers of various levels of expertise. The figures have a good quality for the most part and effectively complement the text to aid in the understanding of their findings.

• Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

I have a few minor suggestions regarding your manuscript's figures:

In figures 1-3, it would be helpful to indicate the number of biological or technical replicates used for the statistical analyses displayed in the plots.

We have added the number of biological replicates for each genotype to our figure legends.

Please consider adding a sentence to the figure legends indicating that the raw data was generated in a previous study.

We have added a sentence indicating that the raw data was generated in a previous study to all relevant figure legends.

Figure 4E may benefit from alternative visualization methods, such as using lines or a different type of plot, to make it easier to distinguish each dataset.

In response to this and other reviewer comments, we have re-formatted Figure 4 to reduce the number of genes displayed in Figure 4E. We believe this greatly increases the readability of the figure and thank the reviewer for their suggestion.

Reviewer #1 (Significance (Required)):

SIGNIFICANCE

===============

• General assessment: provide a summary of the strengths and limitations of the study. What are the strongest and most important aspects? What aspects of the study should be improved or could be developed?

The study is noteworthy for its comprehensive analysis of previously reported data, offering a new understanding of the mechanisms behind the observed robustness of eukaryotic organisms, in particular the active compensation of TDH3 expression. The evidence presented in support of their conclusions is compelling. However, further research is required to investigate the role of active compensation at different regulation levels, in other paralogs, and under different environmental conditions.

• Advance: compare the study to the closest related results in the literature or highlight results reported for the first time to your knowledge; does the study extend the knowledge in the field and in which way? Describe the nature of the advance and the resulting insights (for example: conceptual, technical, clinical, mechanistic, functional,...).

This study provides new insights into the mechanisms of active compensation for the loss of gene expression in yeast. The authors demonstrate that the paralogs TDH1 and TDH2 upregulate in a dose-dependent manner in response to reductions in TDH3, mediated by shared transcriptional regulators Gcr1p and Rap1p. Furthermore, other glycolytic genes regulated by Rap1p and Gcr1p show similar changes in expression, indicating that active compensation of TDH3 by its paralogs is part of a larger homeostatic response. This study provides a mechanistic understanding of active compensation for the loss of gene expression in yeast and has potential implications for other organisms.

• Audience: describe the type of audience ("specialized", "broad", "basic research", "translational/clinical", etc...) that will be interested or influenced by this research; how will this research be used by others; will it be of interest beyond the specific field?

This study may attract a broad audience, as it provides insight into the mechanisms of active paralogous compensation. Their findings have potential implications beyond the yeast's specific field, as they may provide insight into the mechanisms of robustness in other genes and organisms. This research may be of interest in the fields of molecular biology and evolution in particular gene regulation.

• Please define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

My field of expertise is molecular biology and evolution, specifically in the areas of gene duplication, gene expression and regulation, protein evolution, and interaction networks. I am familiar with some of the topics discussed in the paper, such as gene expression and regulation, and have a good understanding of the research related to these topics.

We thank the reviewer for their insightful comments and thorough reading of the manuscript. We believe that the revisions, as described in more detail below, improve the manuscript and we greatly appreciate the suggestions.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

The ms uses RNAseq data on S cerevisiae with TDH3 perturbations (cis and trans) from prior publication to look into RNA expression of TDH3 paralogues and genes within the same pathway. Analysis of both cis and trans TDH3 perturbation data suggests that the compensatory mechanisms (via either the paralogues or the upstream/downstream enzymes of the glycolytic pathway) are dependent on GCR1 and RAP1 transcription factors.

Major comment but OPTIONAL: The RNAseq data presented here convincingly convey the authors claims. Nevertheless, if any of the following data becomes available in the meantime, they will add a lot to the current ms: 1. Protein expression data can independently validate the findings and help support/clarify potential issues emerging from the data on the glycolytic pathway - see 2nd minor comment.

The revised manuscript includes new data showing increased expression of TDH2 upon deletion of TDH3 at the protein level using a TDH2:CFP fusion protein under the control of the native TDH2 promoter and at the native locus (Figure 1B). These protein-level data do indeed independently validate our RNA-seq findings for TDH2. We have also re-arranged Figure 4 and clarified the section of the manuscript describing changes in expression in the rest of the glycolytic pathway to better communicate that these changes in gene expression may or may not be part of an active compensation mechanism (see further discussion below).

1. Any data that show expression of TDH3 as a result of TDH1/TDH2 expression changes occurring independently of Gcr1/Rap1 can support the claims on robustness as a consequence of multiple paralogues being around.

We have RNA-sequencing data for strains in which TDH1 or TDH2 was deleted individually (GSE175398, data from Vande Zande et al., 2022). We saw that in these strains TDH3 expression was not significantly increased. We believe that this finding is most likely due to the difference in basal expression levels between paralogs. TDH3 is expressed at approximately 6x the level of TDH2, and TDH1 is expressed in stationary phase rather than exponential growth as TDH2 and TDH3 are (See new supplementary Figure S1). Deletion or reduction of TDH3 expression represents a much larger change in total GAPDH levels in the cell, and therefore might elicit a much stronger compensation response than deletion of TDH2 or TDH1. We are interested in how the different expression levels, patterns, and enzymatic activity levels have diverged between paralogs and contribute to their relative function in the cell, and, as mentioned above, another member of the Wittkopp lab is currently working on a manuscript addressing these questions in greater detail. For these reasons, we have chosen not to include these data in the current manuscript.

Minor comments

1) Introduction and analysis framing: there seems to be two aspects for robustness and compensation that the manuscript focuses on. The one is through paralogues and the other via alteration in the expression of genes in the same pathway. The study shows both, yet there is particular weight on the paralogues.

The introduction should also mention both in a coherent and organized way. As an example, the second paragraph in the intro refers to 'upregulation of a paralog' in the 1st sentence, then it refers to an example that fits better to compensation through changes in expression of enzymes in the same pathway.

We have adjusted the language in the second paragraph of the introduction to clarify that the other enzymes that are actively compensating for CLV1 or SlCLV3 loss in arabidopsis and tomato are paralogs (pg.2 line 21- pg.3 line 8). In addition, we have adjusted our wording of the final introduction paragraph (pg. 5, lines 11-18), and the final results section (pg. 13, lines 17-23) to better communicate that the other genes are changing as part of a homeostatic response programmed into the regulatory network and may or may not contribute to fitness gains in a TDH3 mutant.

2)Figure 4 results/Discussion: Not unexpectedly, PFK1 and PFK2 (in panels 4D and 4B) have very similar expression profiles with respect to TDH3 expression. (Considering that they are part of the same complex, one would expect that their expression levels should correlate at the very least). Yet, PFK1 did not make the significance cutoff. That can be misleading, so it warrants a comment, either on the respective results section or discussion. For that reason and to make easier comparisons expression data should be shown on the same panel (consolidate 4B and 4D) with significance annotations. It would also be nice to see some commentary in terms of pathway output upon changes in TDH3 expression. It seems as if there is a 'diffused signal' through the whole pathway that compensates for TDH3 perturbations, meaning all enzymes may be compensating to different degrees.

We appreciate these suggestions and have used them to re-arrange Figure 4 to more clearly show the response of genes that function at each step in the glycolytic pathway. As noted in the reviewer’s comment, PFK1 and 2 are nearly identical in their expression profiles. The reason one is not significantly upregulated is that it has a higher variance among replicates than the other, which we now point out explicitly in the figure legend. By grouping these genes together in Figure 4, the similarity of their expression changes is much more obvious.

Reviewer #2 (Significance (Required)):

The study demonstrates an example of paralog-dependent changes in gene expression that contribute to phenotypic robustness. The active paralog compensation is transcription factor-dependent, and the same transcription factors are also responsible for compensatory changes in expression levels of genes in the same pathway. I believe that this is an interesting case showing how a negative feedback mechanism in place to maintain pathway output and contribute to phenotypic robustness, receives and integrates signaling from different components of a pathway, including paralogues. The study relies solely on RNAseq data. Although convincing, protein expression data not only could validate the RNAseq data, but also could give a more accurate view of the respective expression profiles. The study describes a molecular mechanism in pathway regulation with broad interest in basic research. It also has particular interest with respect to paralog evolution and brings up questions on the forces that drive paralog divergence.

We appreciate this reviewer’s comments and suggestions and have added several new figures that use fluorescent fusion proteins to provide a quantitative readout of protein expression levels. Specifically, we have added panels showing increased protein expression of TDH2 fused with CFP upon deletion of TDH3 (Figure 1B). We have also added expression of fluorescent reporter genes driven by the TDH1, TDH2, and TDH3 promoters showing the differences in their expression profiles across population growth stages (Supplementary Figure 1). Finally, we have analyzed fluorescent reporter genes with promoters containing mutated Gcr1p TFBS, which also suggest a dependence of the compensatory upregulation on GCR1p (Figures 2D, 3E).

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

In their preprint titled "Active compensation for changes in TDH3 expression mediated by direct regulators of TDH3 in Saccharomyces cerevisiae" Zande and Wittkopp attempt to delineate the molecular mechanism behind compensation. They have chosen 3 paralogs, TDH1, 2 and 3 in Saccharomyces cerevisiae as their system of choice, building on an earlier study where they have used RNA-seq transcriptomics to characterize how global gene expression is affected by strains harbouring regulatory mutations at the TDH3 locus or a TDH3 gene knockout. The major claims made by the authors in this study are as follows:

1. The TDH1/2/3 system demonstrates compensation, such that changes in levels of expression of TDH3 result in altered expression levels of TDH1 and TDH2

2. The mechanism of this compensation is "active", that is it involves modulating the transcription of paralogs in response to altered TDH3 in the cell. iii. The transcription factors Gcr1 and Rap1 are likely candidates mediating this compensation. The effects of these regulators on TDH1 and TDH2 differ and produces different profiles of compensatory expression for these two genes.

3. Since Gcr1 and Rap1 regulate other genes coding for glycolytic enzymes, compensation is related to altered expression of a larger cohort of genes. Major comments:

4. The authors' claims regarding the roles of Rap1 and Gcr1 as mechanisms of compensation are supported by correlative evidence from RNA seq data. To establish the causal relationships that the authors intend, more directed experiments like the ones listed below are required: i. Monitoring the activity of TDH1 and TDH2 promoters (as YFP-fused reporters) in the various strains

We have added new experimental data to the manuscript monitoring the activity of the TDH1 and TDH2 promoters driving YFP in different phases of the growth curve, demonstrating the divergence in their gene expression patterns (Supplementary Figure 1). Because of the divergence in expression patterns, we chose to focus additional efforts on TDH2 and have added new data showing an increase in expression of a CFP::TDH2 fusion protein upon deletion of TDH3. These new experiments provide strong evidence of the causal relationship between the deletion of TDH3 and an increase in TDH2 expression.

ii. Generating mutant promoter reporters for TDH1, 2 and 3 that are unable to bind to Gcr1 and Rap1 and testing their activity in the various mutant strains

We have added new experimental data to the manuscript demonstrating that increases in the activity of the TDH3 and TDH2 promoters upon deletion of TDH3 are dependent upon Gcr1p transcription factor binding sites, as originally hypothesized. Specifically, the new figure panel 3E consists of flow cytometry data showing that the TDH2 promoter driving YFP expression increases in fluorescence upon deletion of TDH3, but that a comparable increase does not occur when Gcr1p TFBSs in the TDH2 promoter are mutated. In addition, the new figure panel 2D shows that the TDH3 promoter driving YFP no longer increases in activity when a Gcr1 TFBSs is mutated. These new experiments provide strong evidence for the dependence of active compensation by upregulation upon shared transcription factor GCR1.

1. The authors claim that Gcr1 and Rap1 have similar impact on other glycolytic enzymes. However, these conclusions are also based on RNA -seq data and hence remain correlative. Based on the presented results alone, and lack of a molecular mechanism for why the levels of Rap1 and Gcr1 change in TDH3 mutant strains, it may just as easily be argued that the change in expression of other glycolytic enzymes (and therefore glycolytic flux) may be the cause for altered Rap1/Gcr1 activity and not the consequence. To test which of these possibilities are true, I would recommend the following approaches:

i. Promoter reporters for glycolytic enzymes of interest, and mutant versions that don't respond to Rap1/Gcr1

ii. Change glycolytic flux by altering growth conditions (e.g. fermentable/non-fermentable carbon source) and check to see if compensation is altered

While it is possible that mutations in the TDH3 promoter that change TDH3 expression alter the expression of other glycolytic genes, and this in turn alters Rap1/Gcr1 activity, resulting in the upregulation of the TDH paralogs, we believe it is more likely that changes in the activity of Rap1/Gcr1 are a cause rather than a consequence of altered expression of glycolytic genes because it has previously been shown that these genes are under the control of Rap1 and Gcr1. We have adjusted the wording of the final results section, and throughout the paper, to clarify that we believe the similar expression patterns observed for other glycolytic genes suggest that the increase in paralog expression that results in active compensation is part of a larger regulon, which indeed may be responsive to changes in glycolytic flux. We cannot say, however, whether the upregulation of other glycolytic genes is part of the compensatory response per se. We believe this clarification, in addition to the new experiments showing the dependence of TDH3 and TDH2 upregulation on transcription factor binding sites for GCR1, addresses the issues raised above.

Reviewer #3 (Significance (Required)):

This study attempts to address the mechanistic basis for an important homeostatic mechanism, i.e. compensation. Compensation is an almost universal mechanism seen in pathways with genetic redundancy. As pointed out by the authors, compensation ensures that gene regulatory networks produce robust outcomes and are resistant to perturbation. Though compensation is often observed, the mechanistic basis is usually unclear. This study throws light on possible transcriptional mechanisms that orchestrate compensation by altering expression levels of paralogous enzymes. In this regard the study is novel, important, and fills a lacuna in the area. However, in its current form, the study lacks the necessary causal evidence needed to substantiate the claims made by the authors. Further, the mechanism linking transcriptional regulation and metabolic flux is still lacking. As a result, though interesting, the study doesn't provide a complete picture and fails to make an impact.

We thank the reviewer for their comments and believe that the additional experiments and data added to the revised manuscript, including using fluorescent reporter genes and mutant alleles to measure the activity of promoters and show their dependence on RAP1/GCR1 binding sites, provide the causal evidence necessary to make this an impactful study.

Since I am not a yeast geneticist, it is possible that several of the concerns raised by me are due to my lack of knowledge of the system and some of the links that I find missing may have been demonstrated by others. If this is the case, I would suggest that the authors provide adequate background to address these concerns in the manuscript itself. It is my opinion, that this study, once shored up, will be of interest to a wide-readership and could also provide important experimental data that could be used for mathematical modeling.

We appreciate the reviewer’s comments and believe that the changes we’ve made to the manuscript, including the addition of critical new data that complements and supports the RNA-seq data originally presented in the manuscript, does indeed make this a study that will be of interest to a wide readership.

This is news worthy because this is a large election that we will have to think about in the next year. Seeing that we have to figure out who will be the next president people will want to think about counties that may flip to change who the presidential candidate is.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

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Reply to the reviewers

*Reviewer #1 (Evidence, reproducibility and clarity (Required)): *

*In their study, Yamano et al. dissect the mechanism of TBK1 activation and downstream effects, especially in its relation to mitophagy adaptor OPTN. The authors find that OPTN's interaction with ubiquitin and the autophagy machinery, forming contact sites between mitochondria and autophagic membranes, results in TBK1 accumulation and subsequent autophosphorylation. Based on these findings, the authors propose a self-propagating feedback loop wherein OPTN phosphorylation by TBK1 promotes recruitment and accumulation of OPTN to damaged mitochondria and specifically the autophagosome formation site. This formation site is then involved in TBK1 autophosphorylation, and the activated TBK1 can then further phosphorylate other pairs of OPTN and TBK1. A OPTN monobody investigation strengthens their findings. *

*Critique: *

• It would be helpful if the authors could more clearly highlight the previous findings in OPTN-TBK1 relationship and which gaps in the understanding their study addresses.* We thank the reviewer for this comment. As suggested, we have highlighted previous findings and detailed in the Discussion how the study advances our understanding of TBK1 activation.

• It is not always clear whether experiments have been replicated sufficiently; this should be indicated in the figure descriptions.* In the original manuscript, most of the data shown was derived from duplicated experiments. For the revised version, we repeated experiments as needed to generate the replication necessary (i.e, N = 3) for determining statistical significance. Error bars and statistical significance have been added to the graphs and figure legends accordingly.

• During the discussion, references to the figures that indicate conclusions should be added where appropriate.* We thank the reviewer for the suggestion. References to figures have been added were appropriate to the Discussion.

*Figure 1 / Result "OPTN is required for TBK1 phosphorylation and subsequent autophagic Degradation": *

*o In a) the TBK1 and TOMM20 blots feature an image artefact that makes it appear like the blots are stitched together or there was a problem with the digital imager. The quantification in b) seems to be missing replications. *

We found that the artifact came from an automatic pixel interpolation process in Adobe Photoshop when the image was rotated by a small angle. We have provided the original immunoblotting data below as evidence that the data were not stitched from separate images. More accurate representations of the images without the artifact are now shown in Fig1 A of the revised manuscript.

For Fig 1b, the experiment was independently replicated three times with error bars added to each plot on the graph.

*o g) should feature the wt cell line on the same blot for better comparability as well as quantification and replication like done in f) *

As suggested, we have included the WT cell line in the immunoblot (See Fig 1g). In addition, Reviewer 2 asked that we provide data for Penta KO cells without exogenous expression of the autophagy adaptors and expressed concern regarding the lower expression of NDP52 relative to OPTN. To address these issues, we repeated the mitophagy experiments and detected phosphorylated TBK1 in six different cell lines: WT, Penta KO, Penta KO stably expressing OPTN at both low and high expression levels, and Penta KO stably expressing NDP52 at low and high expression levels. Immunoblots of phos-TBK1(pS172), TBK1, OPTN, NDP52, TOMM20, and actin were generated under four different conditions (DMSO, valinomycin for 1 hr, valinomycin for 3 hrs, and valinomycin in the presence of bafilomycin for 3 hrs). In addition, phos-TBK1 abundance in the six cell lines was determined in response to val and baf for 3 hrs and the expression levels of NDP52 and OPTN were similarly determined in response to DMSO. Error bars based on three independent experiments have been incorporated into the data, which are shown in Figure 1g and 1h of the revised manuscript.

*o h) is missing the blots for controls actin and TOMM20 *

Immunoblots for actin and TOMM20 have been added, please see Fig 1i in the revised manuscript.

*o In the text to e/f), the authors write that NDP52 KO effect on pS172 are comparable to controls, though the quantitation in f) indicates that pS172 signal is indeed significantly reduced compared to wt *

The reviewer is correct, the phos-TBK1 (pS172) signal in NDP52 KO cells is reduced compared to that in WT cells, but is only moderately lower in NDP52 KO cells relative to OPTN KO. We regret the error, which has been corrected in the revised manuscript.

*o In the text to h/i), the authors write "there was a significant increase in the TBK1 pS172 signal in cells overexpressing OPTN", though the quantification in i) does not indicate significance levels *

We performed statistical analyses on the phos-TBK1 (pS172) levels between cells with or without OPTN overexpression and have added the degree of significance to Fig 1j. As indicated in the original manuscript, there was a significant increase in phos-TBK1 (pS172) levels when OPTN was overexpressed.

*Figure 2 / Result "OPTN association with the autophagy machinery is required for TBK1 activation": ** o In b), pTBK1 at val 1 hr only features one dot/experiment per cell line *

Three independent replicates of the experiment (val 1 hr) were performed. The levels of phos-TBK1 (pS172), total TBK1, and actin were quantified, and the graph was remade with error bars and statistical significance incorporated. Please see Fig 2b in the revised manuscript.

*o In the text to c), the authors claim that the mutants reduce/abolish the recruitment of OPTN to the autophagosome site. A costain for LC3, as done for SupFig 1b, would be necessary to support that specific claim. *

To address the reviewer’s concern regarding the recruitment of OPTN mutants to the autophagosomal formation site, we performed two different experiments. First, when OPTN WT is recruited to the contact site between the autophagosomal formation site and damaged mitochondria, it should be heterogeneously distributed across mitochondria. In contrast, OPTN mutants that are unable to associate with the autophagosome formation sites should be largely localized to damaged mitochondria since the mutants are still capable of binding ubiquitin. When we examined the mitochondrial distribution of OPTN WT following valinomycin treatment for 1 hr, more than 80% of the Penta KO cells exhibited a heterogeneous distribution, whereas only 10% of the cells showed a similar distribution for OPTN 4LA or OPTN 4LA/F178A (please see Fig 2g in the revised manuscript). Although the OPTN F178A mutant exhibited 50% heterogeneous distribution (Fig 2g), this may be because OPTN F178A retains the ability to interact with ATG9A vesicles. In fact, our previous mitophagy analyses (Keima-based FACS analysis, Yamano et al 2020 JCB), which are strongly correlated with OPTN mitochondrial distribution, showed that the OPTN F178A mutant moderately (~ 60%) induced mitochondrial degradation. This degradation effect was slightly higher (80%) with OPTN WT but significantly lower (9%) with the 4LA/F178A mutant. In the second experiment, Penta KO cells expressing either OPTN WT or the OPTN mutants were immunostained for exogenous FLAG-tagged OPTN, endogenous WIPI2, and HAP60 (a mitochondrial marker) after valinomycin treatment for 1 hr (see Fig 2e and 2f in the revised manuscript). Because LC3B is assembled on the autophagosomal formation site as well as completed autophagosomes, we detected endogenous WIPI2 because WIPI2 is only recruited to autophagosomal formation sites (Dooley et al. 2014 Mol Cell). Confocal microscopy images and their associated quantification data indicate that WIPI2 foci formation during mitophagy was reduced in Penta KO cells expressing the OPTN mutants (4LA, F178A and 4LA/F178A) as compared to Penta KO cells expressing OPTN WT.

*o d) and g) as simple confirmations of KO/KD efficiency might be better suited for the supplemental part, or blots for FIP/ATG be included with the blots in e) and h) *

Based on the reviewer comments, we performed additional experiments related to Figure 2 and have incorporated the new data into the revised figure. The original Figure 2d, e, f, g, h, and I have been moved to supplemental Figure 5.

*o In the text to e), the authors claim that the levels of pS172 in the KO cell lines did not increase during mitophagy, though the blot and quantification in f) seem to indicate an increase. The results therefore don't seem to align completely with the claims that pS172 generation in response to mitophagy requires the autophagy machinery, or that FIP200 and ATG9A rather than ATG5 are critical for TBK1 phosphorylation. *

Although newly generated pS172 TBK1 was reduced in FIP200 KO and ATG9A KO cells relative to WT cells, the signals gradually increased. In the autophagy KO cell lines (FIP200 KO and ATG9A KO), phos-TBK1 accumulates prior to mitophagy stimulation. Although suggesting it is mitophagy-independent, phos-TBK1 accumulation prior to mitophagy stimulation in autophagy KO cell lines complicated interpretation of the results. To avoid this issue, we used siRNA to transiently knock down FIP200 and ATG9A. As shown in the original manuscript (Fig 2g, h, I in the original manuscript, supplementary Fig 5d, e, f in the revised manuscript), knockdown of FIP200 and ATG9A prior to mitophagy induction allowed us to observe mitophagy-dependent phosphorylation of TBK1. This result strongly suggests that the autophagy machinery does induce TBK1 phosphorylation in response to Parkin-mediated mitophagy. However, TBK1 phosphorylation still increases, albeit very slightly, in the FIP200 and ATG9A knock down cells. Thus, it may be reasonable to assume that OPTN-dependent phosphorylation of TBK1 can occur to a certain degree even in the absence of autophagy components. We have noted this in the Discussion.

While conducting experiments for the revised manuscript, we determined that TAX1BP1 is responsible for the accumulation of phos-TBK1 in the autophagy KO cell lines under basal conditions. When TAX1BP1 is knocked down in FIP200 KO or ATG9A KO cells, the basal accumulation of phos-TBK1 was eliminated and then we could observe mitophagy-specific TBK1 phosphorylation (please see Fig 2h, i, j, k in the revised manuscript). These results showed that mitophagy-dependent phos-TBK1 is largely attenuated in FIP200KO and was almost completely eliminated in ATG9A KO cells (Fig 2k in the revised manuscript).

*o f) is missing significance indications. Its description has a typo: "bad" instead of "baf" *

Newly synthesized pTBK1 (pS172) during mitophagy was quantified and statistical significance incorporated into the figure (please see supplementary Fig 5c). The identified typo has been corrected.

*Figure 3 / Result "TBK1 activation does not require OPTN under basal autophagy conditions": *

*o In the text to SupFig2, the authors claim that pS172 levels are significantly elevated, but no significance levels are indicated *

Statistical significance was determined for all proteins shown in original supplementary Fig 2 and the results have been incorporated into the relevant figure. The original supplementary Fig 2 is now supplementary Fig 6.

*o In the text to a), NBR1 is claimed to colocalize with Ub, but no costaining with Ub is shown. The claimed lacking colocalization of OPTN with Ub is not obvious from the images; a quantification might be appropriate. *

Since the anti-NBR1 antibody used in the original manuscript is derived from mouse, we were unable to use it in conjunction with the mouse ubiquitin antibody. Because ubiquitin-positive foci and NBR1-positive foci contain p62 (original Fig 3a) and NBR1 and p62 are known to tightly interact each other (Kirkin et al. 2009 Mol Cell and Sanchez-Martin et al. 2020 EMBO Rep), we stated that "NBR1 colocalizes with Ub". However, the reviewer is correct. To remedy this confusion, we obtained a rabbit anti-NBR1 antibody (a gift from the Masaaki Komatsu group) and used it to co-immunostain with anti-Ub antibodies (please see supplementary Fig 7a of the revised manuscript). NBR1 foci colocalize with both ubiquitin and p62 in FIP200 KO and ATG9A KO cells. Further, based on comments from Reviewer 2, we purchased several anti-TBK1 antibodies and identified one that was able to detect endogenous TBK1 by immunostaining (see Figure 1 for reviewers in our response to Reviewer 2 below). Using this anti-TBK1 antibody, we showed that a part of TBK1 also associates with ubiquitin and p62-positive aggregates.

*o In the text to b), the authors make reference to significant changes, but replication/ quantification/ significance testing is missing. *

We independently performed the same experiments three times. The levels of TBK1, phos-TBK1 (pS172), all five autophagy adaptors, and TOMM20 in both the supernatants and pellets have been quantified with error bars and statistical significance indicated. These results have been incorporated into Figure 3c in the revised manuscript.

*Figure 4b) is missing the pTBK1 data that is referenced in the text. In the text to figure 5 c/d), the authors claim that certain mutants have no significant effect on mitophagy, though d) is missing significance testing *

*Figure 6 c/d/i) appear to be missing replication. *

For Figure 4b, phos-TBK1 was immunoblotted (See Fig 4b of the revised manuscript). For Figure 5b and d, statistical significance was determined for the effect of TBK1 mutations on autophosphorylation and OPTN phosphorylation and the effect of the TBK1 mutants on Parkin-mediated mitophagy. For Figure 6 c/d/I, the experiment was repeated; error bars and statistical significance have been added to the associated graphs.

*Reviewer #1 (Significance (Required)): Removal of damaged mitochondria by the mitophagy pathway provides an important safeguarding mechanism for cells. The Pink1/Parkin mechanism linked to numerous modulators and adaptor proteins ensures an efficient targeting of damaged mitochondria to the phagophore. The Ser/Thr kinase TBK1, in addition of multiple roles in innate immunity, is a major mitophagy regulator as has been revealed by the Dikic and Youle groups in 2016 (Richter et al., PNAS). The mechanistic insights provided by this manuscript add to a growing body of studies of how the autophagy machinery interconnects with cellular signalling networks. Although parts of the results need to be further validated, the data shown is of high quality, revealing an important conceptual advance. The paper is interesting and of general relevance beyond the signalling and autophagy community. *

We would like to thank Reviewer 1 for the comments and suggestions, many of which improved our manuscript. We hope that the reviewer’s comments have been adequately addressed in the revised manuscript.

*Reviewer #2 (Evidence, reproducibility and clarity (Required)): Summary In this manuscript, Yamano and colleagues show that as for Sting-mediated TBK1 activation, Optn provides a platform for TBK1 activation by autophosphorylation and that TBK1 is activated after the interaction of Optn with the autophagy machinery and ubiquitin and not before. They show that TBK1 phosphorylation is blocked by bafilomycine A1, an inhibitor of vacuolar ATPases that blocks the late phase of autophagy. Furthermore, they demonstrate that Optn is require for TBK1 phosphorylation since variation of Optn expression regulates TBK1 phosphorylation in response to PINK/Parkin-mediated autophagy. Interestingly, using immunofluorescence microscopy, they show that Optn forms sphere like structures at the surface of damage mitochondria which are more dispersed in the absence of TBK1. In addition, TBK1 is also recruited at the surface of damage mitochondria and as Optn and NDP52 (but not p62) colocalize with LC3B in response to PINK/Parkin-mediated mitophagy. Next, it is demonstrated that the Leucin zipper and LIR domains of Optn (which modulate Optn interaction with autophagosome) play an important role for TBK1 activation. Additionally, the autophagy core is shown to be required for TBK1 activation. Under basal conditions, depletion of the autophagosome machinery leads to an increase in autophagy receptors (except Optn) and TBK1 phosphorylation which colocalize with ubiquitin in insoluble moieties. In contrast, Optn remains cytosolic and is dispensable for TBK1 activation in these conditions. Then, using the fluoppi technic, the authors demonstrate that the generation of Optn-Ubiquitin condensates recruits and activates TBK1. They express in HCT116 TBK1-deficient cells engineered or pathological ALS mutations of TBK1 that affect ubiquitin interaction, structure, dimerization and kinase activity of TBK1. The expression level of TBK1 was only affected by the dimerization-deficient mutations. None of the mutations impaired Optn and TBK1 ubiquitination. Interestingly, some ALS-associated mutations affect TBK1 activity and it is said in the text that the dimerization-deficient mutations of TBK1 affect its activity proportionally to their level of expression, which is not really correct (the expression level of the mutants is very heterogenous and not always correlate to their activity). Regarding their effect on mitophagy, the authors claim that the phosphorylation of TBK1 correlate with mitophagy which is not really the case. By using TBK1 inhibitor or TBK1-depleted cells, the authors conclude that TBK1 is the only kinase phosphorylating Optn. However, BX-795 is not completely specific to TBK1. Finally, the authors use monobodies against Optn effective in inhibiting mitophagy in NDP52 KO cells. Some of the monobodies have been shown to form a ternary complex with Optn and TBK1, while others compete for the interaction between Optn and TBK1 which involves the amino-terminal region of Optn and the C-terminal region of TBK1. Monobodies that compete for the interaction of Optn with TBK1 could alter the cellular distribution of Optn and inactivate TBK1, but they do not alter the ubiquitination of Optn. Finally, these monobodies inhibit 50% of mitophagy. *

*Major and minor points: Introduction The first paragraph of the Introduction section is confused and difficult to read. First and second paragraphs (page 3 and top of page 4) are dedicated to macroautophagy processes but ended with one sentence on Parkin-mediated autophagy without further introduction, while all processes regarding mitophagy are detailed in the next paragraph. Links between ideas developed are also somewhat missing. For example, in page 6, the three last sequences detailed the phosphorylation of autophagosome component, the fact that Optn and TBK1 genes are involved in neurodegenerative diseases and autophosphorylation of TBK1 as a pre-requirement for TBK1 activation without evident links between them, except "interestingly". *

In response to the reviewer’s suggestion, we have rewritten the Introduction. The first paragraph focused on introducing the molecular mechanism underlying macroautophagy and the second paragraph focused on Parkin-mediated mitophagy. As the reviewer indicated, the ALS mutations and TBK1 phosphorylation during Parkin-mediated mitophagy are not well related, so we moved the background material on the relationship between OPTN and TBK1 in neurodegenerative diseases to the beginning of the section describing Figure 5. We believe these changes have made the Introduction easier to read and understand.

*Results *

*Major points: *

*1- Results are often over-interpreted regarding data obtained leading to inadequate conclusions (see below for details); *

We regret the reviewer’s concerns regarding over-interpretation. To address this issue, we have carefully considered the data, performed additional experiments where necessary, and rewritten the results accordingly. Please see our point-by-point responses below.

*2- Quantification of protein levels detected by western blot are provided as "relative intensities" without referring to specific loading control or to total protein when -phosphorylated forms are quantified (Fig. 1b, 1d, 1f, 1i, 2b, 2f, 2i, 5b, 7b, supplemental figures 2b). *

For the immunoblots, we loaded the same amount of total cell lysate and the phosphorylated forms were quantified relative to the total protein input. This has been mentioned in the Materials and Methods.

*3- In western blotting experiments, authors described slower migrating bands as "ubiquitinated" forms of detected proteins, but never provided experimental evidences that it could be the case. Use of non-specific deubiquitinase incubation of extracts prior to western blot could help to correctly identified ubiquitination versus other post-translational modifications such as phosphorylation, glycosylation, acetylation etc... *

We appreciate the reviewer’s suggestion. The cell lysates after mitophagy induction were incubated in vitro with a recombinant USP2 core domain (non-specific DUB), and then immunoblotted. As shown in supplemental Fig 1 of the revised manuscript, the slower migrating OPTN bands disappeared in a USP2-dependent manner. The slower migrating NDP52 and TOMM20 bands likewise disappeared. These results confirm that the slower migrating OPTN, NDP52, and TOMM20 bands are ubiquitinated.

*4- Conclusions from data obtained by immunofluorescent imaging are often drawn from only one image presented without further statistical analysis. *

Statistical significance was determined for the immunofluorescent data (original figures 1j, 2c and 3a). Please see Fig 1l, 2f, 2g, and 3a in the revised manuscript.

*Page 7: - authors referred to TBK1 phosphorylation induced by mitophagy induction as "TBK1 phosphorylation induced by Parkin-mediated ubiquitination" while mitophagy can be induced independently of Parkin (ex: via mitochondrial receptors) and without any evidence (according to referee's knowledge) of a link between ubiquitination by Parkin and TBK1 phosphorylation. *

As the reviewer indicated, Parkin-independent and ubiquitination-independent mitophagy pathways are also known (i.e. receptor-mediated mitophagy driven by NIX, BNIP3, BCL2L13, FKBP8, FUNDC1, or Atg32). Therefore, references to "mitophagy" in our manuscript were reworded as "Parkin-mediated mitophagy". Since TBK1 phosphorylation is observed before mitochondria are degraded and is dependent on Parkin-mediated ubiquitin (for example, see Fig 1c), we use the phrase "TBK1 phosphorylation triggered by Parkin-mediated OMM ubiquitination".

*Fig 1g: Western blots performed in Penta KO cells without exogene expression of any autophagy receptors should be provided as control. Furthermore, lower expression of NDP52 relative to that of Optn (using flag antibodies) should be discussed as it can explained the differential levels in TBK1 phosphorylation observed. *

As suggested, we repeated the experiment using Penta KO cells in the absence of exogeneous autophagy adaptor expression. Furthermore, we expressed different amounts of NDP52 and OPTN (indicated as low and high in the figure) in Penta KO cells to rule out the possibility that higher TBK1 phosphorylation is induced by simple overexpression of autophagy adaptor (please see Fig 1g and h in the revised manuscript). At high NDP52 expression (2.5-3.0-fold higher than endogenous NDP52), phosphorylated TBK1 was reduced to ~30% the level of that observed in WT cells after 3 hrs with val and baf. In contrast, Penta KO cells with higher OPTN expression (3.0-fold higher than endogenous OPTN) had phosphorylated TBK1 signals that were 2-fold higher than those in WT cells. Based on these results, we concluded that OPTN is an important adaptor for TBK1 activation during Parkin-mediated mitophagy.

*Page 8: Supplemental Fig 1a: - The inability of authors to observe TBK1 endogenous signal in HeLa cells using commercially available antibodies is surprising as many publications reported successful staining (see Figure 1 of Suzuki et al. 2013 Cell type-specific subcellular localization of phospho-TBK1 in response to cytoplasmic viral DNA. PLoS One. 8:e83639 among others) as well as commercial promotion (see Anti-NAK/TBK1 antibody from Abcam reference: ab235253). *

For the original manuscript, anti-TBK1 antibodies purchased from abcam (ab235253), CST (#3013S), Proteintech (28397-1-AP), and GeneTex (GTX12116) for immunostaining were unable to yield TBK1-positive signals (please see Fig 1 for reviewers below). WT and TBK1-/- HCT116 cells stably expressing Parkin were treated with valinomycin for 1 hr and immunostained with the indicated antibodies. Anti-phos-TBK1 antibody (CST, #5483) was used as a positive control. Based on these results, we stated in the original manuscript that the "endogenous TBK1 signal could not be observed using commercially available antibodies". At the reviewer’s suggestion, we purchased anti-TBK1 antibodies from abcam (ab40676) and CST (#38066). As shown in the figure below, the immunofluorescent signals generated by these antibodies were detected in WT, but not in TBK1-/- cells. The CST (#38066) antibody yielded a stronger signal, most of which was on damaged mitochondria. Thanks to this suggestion, we repeated the experiment using the new anti-TBK1 antibody. Furthermore, based on a suggestion from Reviewer 3, we detected mitochondrial recruitment of TBK1 during mitophagy stimulation (valinomycin for 30 min or 2 hrs in the presence and absence of bafilomycin; supplemental Fig 2 in the revised manuscript). We also detected association of endogenous TBK1 with ubiquitin-positive condensates in WT, FIP200KO, and ATG9A KO cells (Fig 3a and supplementary Fig 7a in the revised manuscript).

*- Conclusions of the localization of signal on mitochondria (dispersed, in the periphery or at contact sites) are clearly over-interpreted in the absence of other membrane or autophagosome specific labeling and statistical colocalization analyses of multiple images. It is particularly difficult to assess any difference between Tax1BP1, p62 and NBR1 localization on mitochondria subdomains. *

We previously expressed each FLAG-tagged autophagy adaptor in Penta KO cells and observed their localization during Parkin-mediated mitophagy and found that exogenous FLAG-tagged OPTN and NDP52, but not p62, colocalized with LC3B (Yamano et al 2020 JCB). No one has assessed and compared the localization of all five endogenous autophagy adaptors. Although we still believe that the results (supplemental Fig1 in the original manuscript) are informative for researchers in the autophagy field, we decided to remove that data from the revised manuscript since they are not the main focus of the study. We will consider publishing those data elsewhere in the future after co-staining with autophagosome markers and assessing the statistical significance of colocalization as the reviewer suggested.

*Page 9: *

*- First part of results ended without any conclusions. *

As detailed in the previous response, we have removed results for mitophagic recruitment of autophagy adaptors (supplementary Figure 1 in the original manuscript).

*- The observation that "TBK1 phosphorylation was not apparent in the Optn mutant cell lines, even after 3 hrs of valinomycin, ..." is inconsistent with detection of bands with anti-pS172-TBK1 antibodies in Fig 2a detected at 1hr (with F178A) and 3 hrs (4LA, F178A, and 4LA/F178A mutants) of treatment. *

We apologize for the confusion. This statement was clearly our mistake. We had intended to state when "all autophagy adaptors are deleted" no phosphorylated TBK1 was observed. We have rewritten this part as "TBK1 phosphorylation was not apparent in the Penta KO cells even after 3 hrs with valinomycin".

*- Similarly, decreased levels of phosphorylated TBK1 stated for F178A mutant was only observed at 1 but not 3hrs or at 3hrs in the presence of bafilomycin. *

Based on the mitophagy assay previously reported (Yamano et al 2020 JCB), the F178A mutant only moderately inhibited mitophagy (60% mitophagy with the F178A mutant vs 80% mitophagy with OPTN WT). Conversely, the 4LA mutant and 4LA/F178A double mutant had stronger inhibitory effects on mitophagy (35% for 4LA and 9% mitophagy for 4LA/F178A). Therefore, the levels of phos-TBK1 after 1 hr with valinomycin or 3 hrs with valinomycin in the presence of bafilomycin are consistent with mitophagy progression. When mitophagy proceeds efficiently, the amount of phos-TBK1 in the 1 hr val samples is reduced relative to the 3 hr val samples due to autophagic degradation.

To more clearly observe and compare the levels of mitophagy-dependent phos-TBK1 among Penta KO cells expressing OPTN WT and the mutants, we treated cells with valinomycin in the presence of bafilomycin for 0, 0.5, 1, and 2 hrs and quantified phos-TBK1. The results are shown in Fig 2c and d in the revised manuscript. The phos-TBK1 signal increased over time with val and baf treatment in all OPTN expressing cells. Cells with OPTN WT generated the most phos-TBK1, whereas the signal generated by the F178A mutant was 75% that of the OPTN WT-expressing cells and the 4LA and 4LA/F178A mutants were about 40%. The experiments were independently replicated three times and error bars and statistical significance were incorporated into the associated graph. These results indicate that OPTN association with the autophagy machinery, in particular ATG9A vesicles, is important for TBK1 activation.

*Page 10: *

*The results and their repartition between figure 2 d, e, f, g, h, I and figure 3 is a bit confusing. In these experiments, it is shown Figure 2 that the absence or depletion of the autophagy machinery increase the phosphorylation of TBK1 and in Figure 3 it is shown that not only the phosphorylation of TBK1 accumulate but also the expression of NDP52, Tax1BP1 and p62. Is it because their degradation by autophagy is blocked (like for phosphoTBK1)? *

The reviewer is correct that autophagy adaptors other than OPTN (especially TAX1BP1, p62 and NBR1) are constantly degraded by macro/micro autophagy (Mejlvang et al. 2018 J Cell Biol and Yamano et al. 2021 BBA Gen Subj). Therefore, these adaptors accumulate in autophagy deficient cell lines (original Fig 3). In this study, we found that in the absence of mitophagy stimulation phos-TBK1 accumulates in autophagy deficient cell lines. This suggests that the accumulated autophagy adaptors induce TBK1 phosphorylation under basal conditions. In the original manuscript, we claimed that TBK1 phosphorylation under basal conditions does not require OPTN since in FIP200 KO and ATG9A KO cells it did not accumulate and did not primarily colocalize with ubiquitin- and TBK1-positive foci (original Fig 3). To gain more direct evidence for the revised manuscript, we performed additional experiments and discovered that TAX1BP1 is the adaptor responsible for TBK1 autophosphorylation under basal autophagy. We treated FIP200KO and ATG9A KO cells with siRNAs against OPTN, NDP52, TAX1BP, p62, and NBR1, and immunoblotted total cell lysates with an anti-phos-TBK antibody. As shown in Fig 3f in the revised manuscript, TAX1BP1 siRNA treatment decreased phos-TBK1 levels without affecting total TBK1. This result indicates that the accumulation of TAX1BP1 in the FIP200 KO and ATG9A KO cells induced TBK1 autophosphorylation under basal conditions. Considering this result, we treated WT, FIP200 KO, and ATG9A KO cells with TAX1BP1 siRNA, and then induced Parkin-mediated mitophagy with valinomycin in the presence of bafilomycin. This strategy eliminated the basal accumulation of phos-TBK1 and allowed us to focus on mitophagy-dependent TBK1 phosphorylation. Please see revised Fig 2h, I, j, and k. The results showed that mitophagy-dependent phos-TBK1 is predominantly attenuated in FIP200 KO and ATG9A KO cells. In Figs 2 and 3, we would like to emphasize that OPTN is required for TBK1 phosphorylation in response to Parkin-mediated mitophagy, whereas TAX1BP1 is required for TBK1 phosphorylation in basal autophagy. Since Reviewer 3 commented that interpretation of the data in original Figs 2d, e, and f was challenging, we elected to move those results to the supplemental figures. We have incorporated the newly acquired data (mitophagy using FIP200 KO or ATG9A KO with TAX1BP1 siRNA cells) into the main figure. We believe that this makes the text easier for readers to understand.

*- Fig 2c: conclusions on *

*the reduction of recruitment of Optn mutants on autophagosome formation seem over-interpreted as: *

*1- no labeling with LC3 has been used to identified autophagsome, *

*2- immunofluorescent signals observed with mutants are dispersed throughout the entire mitochondria network (see the merged images) rendering impossible to distinguish between autophagosome-associated mitochondria and others. *

*The following conclusive sentence stating that association of Optn to damaged mitochondria is not sufficient for TBK1 activation based solely on IF of figure 2c seems therefore unrelated to the obtained data. *

To address concerns about the recruitment of OPTN mutants to the autophagosome formation site, we performed additional experiments. Penta KO cells and those expressing OPTN WT and mutants were treated with valinomycin for 1 hr, and FLAG-tagged OPTN, endogenous WIPI2, and HAP60 (mitochondrial marker) were detected by immunostaining. We detected endogenous WIPI2 because WIPI2 is recruited only to autophagosome formation sites (Dooley et al. 2014 Mol Cell), whereas LC3B assembles on autophagosome formation sites and is also associated with completed autophagosomes. Confocal microscopy images showed that cup-shaped OPTN WT that had been recruited to damaged mitochondria colocalized with WIPI2. Quantification further showed that during mitophagy the number of WIPI2 foci seen in cells expressing OPTN WT decreased in Penta KO cells and cells expressing OPTN mutants (4LA, F178A and 4LA/F178A). These data are shown in Fig 2e and f in the revised manuscript. In addition, we quantified the number of cells that either exhibited heterogeneous or homogeneous recruitment of OPTN to damaged mitochondria after treatment with valinomycin for 1 hr. More than 80% of Penta KO cells with OPTN WT had heterogeneous OPTN recruitment, whereas this distribution was only present in 10% of cells expressing either OPTN 4LA or OPTN 4LA/F178A. Although cells expressing the OPTN F178A mutant exhibited 50% heterogeneous recruitment, this may be because the mutant can interact with ATG9A. As mentioned above, our previous mitophagy analyses (Keima-based FACS analysis, Yamano et al 2020 JCB) showed that the OPTN F178A mutant induced ~60% mitochondrial degradation (which is correlated strongly with OPTN distribution), whereas it was 80% with OPTN WT and 9% with 4LA/F178A.

*- Fig 2d: authors should explain why ATG KO cells displayed lipidated LC3B in the absence of efficient autophagy processes. *

We thank the reviewer for the suggestion. We added the following sentence to explain the function of ATG5 in LC3B lipidation. "Since LC3B lipidation is catalyzed by ATG5, but not FIP200 and ATG9A, the lipidated form disappears only in ATG5 KO cells (Hanada et al 2007 J Biol Chem). "

*- Fig 2e: despite authors statement that TBK1 phosphorylation did not increase during mitophagy in ATG KO cells, increased pS172-TBK1 is visible in FIP200 and ATG5 KO cells especially between 1 and 3 hrs of stimulation, leading to inaccurate conclusions that TBK1 phosphorylation requires the autophagy machinery. Therefore, overall assumption that both ubiquitination and autophagy subunits are required for TBK1 autophosphorylation appears erroneous. *

As the reviewer indicated, phos-TBK1 levels gradually increased in ATG KO cells. The main text was rewritten to more accurately reflect this increase. Based on experiments using the monobodies and those conducted during the revision process, it is apparent that although the autophagy machinery may not be completely essential for TBK1 phosphorylation, it clearly facilitates TBK1 phosphorylation in response to Parkin-mediated mitophagy.

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*- Fig 3a: conclusion that Optn signal is more cytosolic and did not localize with Ub condensates seems speculative as based on: *

*1- only one immunofluorescence image without statistical analysis *

*2- Optn and Ub signals are lower in images with Optn is analyzed compared to other images in which NDP52, TAX1BP1 and NBR1 are detected. *

To address these concerns, we compared and quantified the signal intensities of all endogenous autophagy adaptors in FIP200 KO and ATG9A KO cells. The quantification data are shown in Fig 3a and the immunofluorescence images are shown in supplementary Fig 6a of the revised manuscript.

*- Fig 3b: interpretation of western blot data is uncertain due to lack of appropriate loading control, especially with pellets (P) extracts. In addition, it is not clear how to conclude from the experiments in Fig 3b that autophagy adaptors other than Optn mediate TBK1 phosphorylation. *

When autophagy is inhibited, p62 accumulates in the cytosol as aggregates (Komatsu et al. 2007 Cell). Therefore, p62 should be a positive control. Indeed, Fig 3b in the original manuscript (Fig 3b and c in the revised manuscript) showed that the amount of p62 in the pellet fraction was elevated in FIP200 KO and ATG9A KO cells. Furthermore, these aggregates were also observed in the imaging data (Fig 3a and supplementary Fig 7 in the revised manuscript). As the reviewer indicated, the original manuscript did not clarify whether autophagy adaptors other than OPTN mediated TBK1 phosphorylation; however, our revised results clearly demonstrate that TAX1BP1 is the adaptor responsible inducing TBK1 autophosphorylation when basal autophagy is impaired (please see Fig 3f in the revised manuscript).

*Minor point: reference is missing in the last sentence of the paragraph stating that K48-linked chains dominate when autophagy pathways are impaired. *

While several autophagy adaptors preferentially interact with K48-linked ubiquitin chains (Donaldson et al. 2003 PNAS etc), TRAF6 is recruited to ubiquitin-condensates via p62-mediated K63-linked ubiquitination (Linares et al. 2013 Mol Cell). Furthermore, K33-linked ubiquitin chains are also present in p62-positive condensates (Nibe et al. 2018 Autophagy). Because it’s not clear which ubiquitin-linkage is dominant in the condensates, we decided to delete the sentence. We regret the confusion.

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*Conversely to Optn, they find that the other autophagic receptors localize in insoluble fractions (what does it mean?) independently of TBK1 expression (experiments with DKO cells) and also independently of Optn (where is this shown?). Altogether, these experiments are far from the message of the manuscript. The title of the paragraph "TBK1 activation does not require Optn under basal autophagy conditions" is not correct because even if the level of expression of autophagic receptors and TBK1 phosphorylation are increase in response to the depletion of the autophagy machinery, it does not increase autophagy. *

According to the suggestion, we changed the title of the paragraph to "TAX1BP1, but not OPTN, mediates TBK1 phosphorylation when basal autophagy is impaired." In addition, we rewrote this section.

*- Fig 3d: authors should mention the nature of the upper band observed in Optn western blot and show the same experiment in since solely TBK1 depleted cells since they stated that "electrophoretic migration of Optn was not affected by TBK1 deletion". In addition, suggesting from these sole experiments that "NP52, TAX1BP1, p62, NBR1 and AZI2 form Ub-positive condensates where TBK1 is activated" seems over-interpretated. *

Reviewer 3 suggested we characterize the upper band in the OPTN blot (Fig 3d in the original manuscript). To determine if the band is genuine OPTN, we used phostag-PAGE to analyze cell lysates from cells treated with control siRNA or OPTN siRNA and found that both the lower and upper bands were OPTN species (please see "Figure 2 for reviewers" in our response to Reviewer 3). The same pattern was reported by the Wade Harper group (Heo et al. 2015 Mol Cell). They showed that the OPTN double band pattern on phos-tag PAGE was not affected by TBK1 deletion. We have cited this literature where appropriate in the revised manuscript. In WT cells, it is difficult to detect phosphorylation of autophagy adaptors by TBK1 because basal autophagy constantly degrades them. That’s why we used autophagy KO cell lines.

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*- Fig 4: TBK1 phosphorylation was analyzed in Fig4d and not in Fig4b as stated. In addition, it is rather difficult to conclude from artificial multimerization experiments, as the authors have done, that interaction between Optn and autophagy components contributes to Optn multimerization in genuine conditions. *

Detection of phos-TBK1 has been corrected to Fig 4b. Although artificial, the fluoppi assay provides insights into how OPTN activates TBK1 and how the autophagy machinery contributes to TBK1 activation via OPTN. To determine if artificial OPTN multimerization could bypass the autophagy machinery requirement, we used the fluoppi assay. This assay was important for us to conclude that the autophagy machinery and Parkin-mediated ubiquitination allow OPTN to be assembled in close proximity to where TBK1 is activated. The main text was rewritten to better convey the benefits of the fluoppi assay.

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*This work could have therapeutic consequences but the pathological mutants of TBK1 used affect ALS (Figure 5) while in the discussion it is proposed that monobodies could have a therapeutic interest in familial forms of glaucoma due to the E50K mutation of Optn. It should be better to target only one pathology. *

Both TBK1 and OPTN are causative genes for ALS and many pathogenic mutations are known to impact their function. In this study, we focused on ALS mutations in TBK1 that affect self-dimerization and investigated their impact in response to Parkin-mediated mitophagy. We created the monobodies as a tool to physically inhibit OPTN assembly at the contact site. Although our monobodies inhibit Parkin-mediated mitophagy, they would not be a useful therapeutic strategy for ALS due to the loss of function with the TBK1 mutations. However, because TBK1 E50K is a glaucomatous mutation that causes OPTN-TBK1 to bind more tightly, our monobodies might be applicable to glaucomatous pathology since they could disrupt this interaction. We thus feel that it is appropriate to mention the potential of the monobodies and their future utility in the Discussion.

*- Fig 5c, d: Authors stated that degree of TBK1 autophosphorylation correlated with OPTN phosphorylation at S177 whereas phosphorylated TBK1 is unaffected by L693Q and V700Q mutants that display decreased phosphorylated Optn In addition, authors interpretation of Figure 5 data is clearly problematic as they stated that: *

*1- neither 693Q and V700Q mutants had "significant effect on mitophagy", while decreasing efficiency from 78% to 37-51% *

*2- but conclude that 49.7% mitophagy levels of R357Q mutant is significant mitochondrial degradation. *

*Overall conclusion that mitophagy efficiency is correlated with phosphorylated TBK1 levels is therefore inaccurate. *

We regret that this section did not sufficiently describe the data. Reviewer 3 also noted that the text referencing Fig 5 was difficult to interpret. One of the reasons for the complicated data interpretation is the number of TBK1 mutants used. The L693Q and V700Q mutations used by Li et al. (2016 Nat Commun) were expected to inhibit Parkin-mediated mitophagy since those authors reported that the mutations prevented interactions with OPTN. However, our in-cell assay showed that the two mutations only moderately affected Parkin-mediated mitophagy. Furthermore, both the L693Q and V700Q mutations were engineered based on the X-ray structure, rather than being authentic pathogenic ALS mutations. To avoid any potential confusion, we decided to remove the L693Q and V700A data. We have re-evaluated the other data and have rewritten this section accordingly. Please see the revised main text.

*Discussion *

*Minor points: *

*page 20: - reference is missing in the sentence "Optn cannot oligomerize on its own on ubiquitin-decorated mitochondria". *

We have provided the appropriate reference.

*Major points: *

*Authors stated that they showed that Optn recruitment to damaged mitochondria, itself, is insufficient for TBK1 autophosphorylation, but did not show experiment of Optn recruitment to mitochondria and its consequences on TBK1 phosphorylation in the absence of mitophagy induction signal. Authors could for example target HA-Ash-6Ub to mitochondria in order to artificially recruit hAG-Optn to "ubiquitinated" mitochondria in the absence of mitophagy signal. *

We showed that the efficiency of TBK1 autophosphorylation was reduced in cells expressing the OPTN 4LA/F178A mutant, which cannot interact with the autophagy machinery (Fig 2c and d in the revised manuscript). Cells with FIP200 or ATG9A knockdown also have reduced phos-TBK1 (pS172) as shown in supplementary Fig 5e and f. The rate of phos-TBK1 (pS172) generation in ATG9AKO cells during Parkin-mediated mitophagy is reduced relative to that in WT cells (Fig 2j and k). Since a small amount of phos-TBK1 was generated in both ATG9A knockdown and KO cells (supplementary Fig 5e, f, Fig 2j and k), we concur that it would be premature to conclude that phosphorylation of TBK1 does not occur at all when autophagy core components are absent. A small amount of phos-TBK1 may be generated by OPTN that is freely distributed on the outer mitochondrial membrane. In the revised manuscript, we mention the possibility that TBK1 might be phosphorylated by OPTN independent of the autophagy machinery and were careful to avoid over-interpretation.

As shown in Fig 4, fusing OPTN with an Azami-Green tag can induce artificial multimerization and trigger the generation of phos-TBK1 (pS172). Therefore, we expect that mitochondria-targeted HA-Ash-6Ub would induce TBK1 phosphorylation in a hAG-OPTN-dependent manner as was observed with cytosolic HA-Ash-6Ub (Fig 4). The accumulation of OPTN at the contact site in Parkin-mediated mitophagy is important for TBK1 phosphorylation. Even if OPTN is forced to anchor to the mitochondria, this would induce isolation membrane formation and subsequent autophosphorylation of TBK1. Therefore, the utility of forcing OPTN to anchor to mitochondria is questionable.

*Similarly, experimental approaches used by authors lack dynamics parameters to conclude on formation and elongation of isolation membranes and contacts sites that could be probably obtained through video microscopy. *

Based on the reviewer’s comment, we performed time-lapse microscopy to observe OPTN recruitment to the contact site and followed its movement along with the elongation of isolation membranes during Parkin-mediated mitophagy. HeLa cells stably expressing GFP-OPTN and pSu9-mCherry (a mitochondrial marker) were treated with valinomycin (please see Fig 2l in the revised manuscript). Initial recruitment of GFP-OPTN near mitochondria was evident as small dot-like structures that then elongated over time to become cup-shaped structures and culminated in the formation of spherical structures. Considering the colocalization of OPTN with WIPI1/WIPI2 (markers of autophagosome formation site) in Fig 2e and supplementary Fig 2a, the time-lapse images strongly suggest that OPTN assembles at contact sites followed by elongation in tandem with isolation membranes during Parkin-mediated mitophagy.

*Finally, the model proposed by the authors does not take into account data showing that Optn basally interacts with ubiquitinated mitochondria and LC3 family members (see Wild et al., Phosphorylation of the autophagy receptor optineurin restricts Salmonella growth. Science. 2011 333:228-33), although at lower levels compared to induced conditions, relativizing the impact of the proposed model. *

According to the Reviewer 2 comment, we again read the Science paper (Wild et al. 2011) but could not find data showing that OPTN basally interacts with ubiquitinated mitochondria. At least, we think that under steady state conditions without mitophagy induction, mitochondrial ubiquitination and mitochondrial localization of OPTN are undetectable as shown in supplementary Figure 2 in our revised manuscript.

*In conclusion, this manuscript represents a lot of work but the experiments often lack controls and are over-interpretated. *

***Referees cross-commenting** *

*In my opinion, what emerges from these 3 reviews is that the results lack controls or have not been repeated enough to support the message that the interaction of Optn with ubiquitin and the ubiquitination machinery is sufficient to activate TBK1. In particular, as reviewer 1 says, the phosphorylation kinetics shown in Figure 1a are not consistent with TBK1 phosphorylation following the interaction of Optn with the ubiquitination machinery and ubiquitin. In Figure 1e, there is a decrease in TBK1 phosphorylation in contrast to WTcells as mentioned by Reviewer 1. In agreement with Reviewer 1, we believe that the WT cells are missing in Figure 1g. *

*With regard to Figure 2c, we agree with reviewer 1 that an LC3 label is missing in order to be able to interpret the data. In Figure 2e and f, we agree with reviewer 1 that it is difficult to understand why TBK1 phosphorylation increases in the absence of the autophagy machinery (FIP200 KO and ATG5KO). In Figure 3, loading controls are missing for 3b and c. The TBK1 KO cells alone are missing in Fig 2d. In Figure 2b, pTBK1 is missing. In agreement with reviewer 3, we believe that the data with fluoppi contradict the message of the manuscript since they show that TBK1 can be phosphorylated by ubiquitin in the absence of the ubiquitination machinery. In agreement with reviewer 3, we believe that the experiments in Figure 5 are very difficult to interpret. The first reviewer is right to ask the question of the replicates for figures 6c and d. *

We appreciate the summary of the reviewers’ comments. To address their concerns, we have included the appropriate controls and included the results of three independent experiments in the graphs, which now include appropriate error bars and statistical significance. Thus, we believe we have answered the most critical comments concerning the lack of controls.

In Fig 1a, phos-TBK1 was maximal following 30 min of valinomycin treatment. We confirmed using microscopy-based observations that recruitment of endogenous TBK1 and OPTN and the generation of phos-TBK1 and phos-OPTN at contact sites (marked by WIPI1) near damaged mitochondria was also maximal after 30 min of valinomycin treatment (supplementary Fig 2 and 3). Therefore, the kinetics of phos-TBK1 and phos-OPTN generation are consistent with the recruitment of OPTN-TBK1 to the contact site.

The data presented in Fig 2 clearly indicate that the autophagy components are involved in phos-TBK1 generation during Parkin-mediated mitophagy. Therefore, the claim that ubiquitination machinery is sufficient for TBK1 activation is incorrect. Although we agree that the autophagy gene deletions cannot completely inhibit TBK1 autophosphorylation, mitophagy-dependent generation of phos-TBK1 is largely impaired by ATG9A KO (Fig 2j and k). Thus, there is no doubt that isolation membrane formation is important for TBK1 activation following Parkin-mediated mitophagy.

Fig 1e - The reviewer is correct that phos-TBK1 is reduced in the NDP52 knockout. We have rewritten the main text. It is also true that NDP52 has a smaller effect on TBK1 autophosphorylation as compared to OPTN.

Fig 1g - Immunoblots using total cell lysates prepared from six different cell lines (WT, Penta KO alone, Penta KO stably expressing low or high OPTN or NDP52) under four different conditions (DMSO, valinomycin 1 hr, valinomycin 3 hrs, valinomycin + bafilomycin 3 hrs) showed that OPTN is a rate-limiting factor for TBK1 phosphorylation. Please see Fig 1g and h in the revised manuscript

Fig 2c - The recruitment of OPTN WT and associated mutants to the contact site was re-examined by immunostaining with WIPI2 labeling. We found that OPTN WT was both efficiently recruited to and formed the contact site. In contrast, the OPTN 4LA/F178A mutant was unable to interact with FIP200/LC3/ATG9A and was uniformly (i.e. homogenously) distributed on damaged mitochondria with the rate of autophagosome site formation reduced. Please see Fig 2e, f, g in the revised manuscript.

Fig 2e and f - KO of the autophagy core components FIP200 and ATG9A increased phos-TBK1 under basal, non-mitophagy-associated conditions (see Fig 3). The levels of autophagy adaptors other than OPTN also increased in FIP200 KO and ATG9A KO cells. Furthermore, as shown in Fig 3a and supplementary Fig 7, both phos-TBK1 and the autophagy adaptors accumulated in Ub-positive condensates. Based on previous reports (Mejlvang 2018 J Cell Biol), TAX1BP1, p62, and NBR1 have short half-lives and are quicky degraded by macro/micro autophagy. The accumulation of phos-TBK1 in the absence of autophagy occurs because autophagy-dependent degradation of TAX1BP1 (and other adaptors) is inhibited. This allows for the formation of Ub-positive condensates, which brings TBK1 into sufficient proximity for activation. This has been noted in the revised manuscript.

Fig 3b and 3c - We wonder if the "loading controls are missing for Fig 3b and 3c" statement might be a misinterpretation by the reviewer as TOMM20 was used as the loading control in the original Fig 3b. It was recovered in the supernatant fractions of WT, FIP200 KO, and ATG9A KO cells, indicating that the accumulation of autophagy adaptors in the pellet fractions depends on autophagy gene deletion. Similarly, actin and TOMM20 were used as loading controls in the original manuscript Fig 3c.

Fig 2d (perhaps meant to be Fig 3d) – A previous study reported that phos-tag PAGE blot of OPTN in TBK1 KO cells alone revealed no differences between WT and TBK1 KO cells (Heo et al 2015 Mol Cell). We cited this reference in the revised manuscript.

Fig 2b (perhaps meant to be Fig 4b) - Immunoblots of phos-TBK1 have been incorporated into the results of Fig 4b in the revised manuscript.

Fig 4 - We show in Fig 2 that induction of Parkin-mediated mitophagy promotes OPTN accumulation at contact sites formed by isolation membranes and ubiquitinated mitochondria, and that autophagy core subunits are required for efficient generation of phos-TBK1. Fig 3 shows that phos-TBK1 accumulates in Ub-positive condensates with TAX1BP1, rather than OPTN, and that it is responsible for phos-TBK1 accumulation. Together, these results suggest a model in which TBK1 is activated when OPTN and TBK1 are positioned near each other. We hypothesized that if we could force OPTNs into close proximity the autophagy machinery requirement for TBK1 activation might be bypassed. To assess this model, we designed the fluoppi assay shown in Fig 4. This assay was critical in that it provided an important clue for the molecular mechanism that OPTN and the autophagy machinery use to cooperatively induce TBK1 trans-autophosphorylation. Because the original manuscript may not have sufficiently conveyed our reasoning for the fluoppi analysis, we have rewritten this section. The main point of the fluoppi assay is that engineered OPTN multimerization was able to bypass the autophagy requirement for TBK1 activation.

Fig 5 - For easier interpretation, the L693Q and V700Q data, which are not related to ALS pathology, have been removed.

Fig 5d – Statistical significance has been determined for the mitophagy results and the main text has been rewritten for better clarity.

Fig 6c, d, and I – The experiments were independently replicated more than three times with statistical support and error bars incorporated into the associated graphs.

*Reviewer #2 (Significance (Required)): *

*this manuscript represents a lot of work but the experiments often lack controls and are over-interpretated. The manuscript is for a broad audience. *

For the revised manuscript, additional experiments were carefully performed with appropriate controls and the manuscript was rewritten to address concerns regarding over-interpretation. We hope that we have adequately addressed the reviewer’s comments.

*Reviewer #3 (Evidence, reproducibility and clarity (Required)): *

*The authors investigated the mechanisms by which TBK1 is phosphorylated and thus activated in PINK1/Parkin-mediated mitophagy. They show data indicating that OPTN, by interacting both with ubiquitin-coated mitochondria and with the autophagy machinery, provides a platform where OPTN-bound TBK1 can be hetero-autophosphorylated by adjacent TBK1. *

*According to the prevailing model (prior to this manuscript), TBK1 activation via autophosphorylation leads to TBK1-mediated phosphorylation of OPTN S177 and subsequent pOPTN-mediated recruitment of autophagic isolation membranes to the mitochondria. However, based on the model provided in this manuscript, OPTN needs to interact first with both autophagic membranes and ubiquitin before TBK1 can become activated. *

*This is an important topic. Overall, the experimental data are of high scientific quality. For the most part, the manuscript is clearly written. The figures have been made with great care. The novel insights are relevant. However, a number of issues need to be addressed or clarified. *

*Major comments: *

• Fig. 1a-b shows that pTBK1 (pS172) formation already peaks after 30 min of valinomycin. Even when bafilomycin is added, pTBK1 level already reaches a near maximum after 30 min of valinomycin. If the model proposed by the authors is correct and pTBK1 (pS172) formation requires extensive interaction of OPTN with both ubiquitin and autophagic isolation membranes, they should be able to show (by immunostaining) that OPTN already extensively forms peri-mitochondrial cup/sphere-shaped structures that colocalize with isolation membrane markers after only 30 min of valinomycin. In the present manuscript, they only show formation of such structures after 1-3 h of valinomycin.* We thank the reviewer for the critical comments. Based on the suggestion, we performed immunostaining to observe the recruitment of TBK1 and OPTN to damaged mitochondria as well as the generation of phos-TBK1 (pS172) and phos-OPTN (pS177). HeLa cells stably expressing Parkin and 3HA-WIPI1 were treated with valinomycin for 30 min, and then TBK1, OPTN, phos-TBK1, and phos-OPTN were immunostained along with 3HA-WIPI1 (a marker of the autophagosome formation site) and TOMM20 (a mitochondria marker). Please see supplementary Fig 2a and 3a in the revised manuscript. The TBK1, OPTN, phos-TBK1, and phos-OPTN signals formed dot-like, cup-shaped, and/or spherical structures, most of which were peri-mitochondrial and colocalized with 3HA-WIPI1. In separate experiments, HeLa cells stably expressing Parkin were treated with valinomycin in the presence or absence of bafilomycin for 30 min or 2 hrs and then immunostained. Please see supplementary Fig 2b in the revised manuscript. After 30 min valinomycin in the absence of bafilomycin, many TBK1 and OPTN signals were observed on damaged mitochondria. These signals were quantified from more than 160 cells for each of the four conditions. Each microscopic image generated contained 18-36 cells and corresponds to one dot in supplementary Fig 2c. Based on these results, the abundance of TBK1 and OPTN on mitochondria after 30 min of valinomycin was much higher than that after 2 hrs with valinomycin (supplementary Fig 2c). Similar results were obtained for phos-TBK1 and phos-OPTN (supplementary Fig 3b and c). These results are consistent with the immunoblot data (Fig1a and b).

Furthermore, we show that Parkin expression levels affect the amount of phos-TBK1 generated during mitophagy. Please see supplementary Fig 4 in the revised manuscript. When PARKIN was integrated into HeLa cells under a CMV promoter via an AAVS1 (Adeno-associated virus integration site 1)-locus, the resultant cell line (referred to as high-Parkin) had higher Parkin levels than HeLa cells in which PARKIN was introduced by retrovirus infection (referred to as low-Parkin). In high-Parkin HeLa cells, phos-TBK1 levels reached a maximum after 30 min with valinomycin, while in low-Parkin HeLa cells, phos-TBK1 levels were comparable after 30 min and 1 hr. High-Parkin HeLa was used for Fig 1a, b, c, and d as well as supplementary Fig 1, 2, 3 and 4. For all other Figs, PARKIN genes were introduced by retrovirus infection. This is one of the reasons why val was used for 30 min in Fig1, but 1-3 hrs for the other Figs. Because 3 hrs valinomycin treatment may be unsuitable for evaluating OPTN recruitment to mitochondria/isolation membrane contact sites, we deleted the original Fig 2c and replaced it with the val 1 hr data (Please see Fig 2e in the revised manuscript).

• The authors propose that OPTN needs to interact both with ubiquitin on mitochondria and with isolation membrane proteins such as ATG9A to allow TBK1 phosphorylation. However, their fluoppi experiments in Fig. 4 seem to contradict this. In the fluoppi experiments, the authors generate multimeric OPTN-Ub foci and this is apparently sufficient to induced TBK1 phosphorylation at S172 (shown in 4d,f). In this experiment, there is no induction of autophagy or formation of isolation membranes, and TBK1 nevertheless gets activated.*

Figure 2 demonstrates that both ubiquitin on mitochondria and formation of the isolation membranes are needed to provide a platform for OPTN to assemble in close proximity to each other and subsequently induce TBK1 autophosphorylation. To determine if OPTN proximity is sufficient for TBK1 autophosphorylation (i.e., if engineered OPTN multimerization can bypass the autophagy machinery requirement for TBK1 autophosphorylation), we used the fluoppi assay. The results clearly showed that engineered OPTN multimerization induced TBK1 autophosphorylation without the need for the autophagy machinery. Although this is not a mitophagy experiment, the fluoppi assay provided crucial insights into the molecular mechanism underlying OPTN-mediated TBK1 autophosphorylation. The main text was rewritten to provide more clarity regarding the purpose of the fluoppi experiments.

• Can the authors be more concrete/specific in the discussion about the molecular mechanisms that explain why this 'platform' that is created by OPTN-autophagy machinery interactions is so crucial for TBK1 activation? If I understand the model in Fig. 7D correctly, the OPTN-autophagy machinery interactions are mainly important because they reduce the distance between OPTN-bound TBK1 molecules so that they can trans-phosphorylate each other. But if TBK1 autophosphorylation was just a matter of proximity between OPTN-bound TBK1 molecules, interaction of OPTN with densely ubiquitinated mitochondria should already be sufficient for TBK1 phosphorylation. When multiple OPTN molecule bind to one ubiquitin chain or to closely adjacent ubiquitin chains (similar to the fluoppi experiments), TBK1 molecules binding to OPTN would be expected to be already closely enough to one another for trans-autophosphorylation.*

The amount of phos-TBK1 during Parkin-mediated mitophagy was reduced in cells with the OPTN 4LA/F178A mutant, which cannot interact with the autophagy machinery (e.g. FIP200, ATG9A, and LC3) but can be targeted to mitochondria (see Fig 2c, d). ATG9AKO cells also had reduced amounts of phos-TBK1 relative to WT cells (See Fig 2j, k). Therefore, rather than OPTN-ubiquitin freely diffusing laterally on the outer membrane, we suggest that the contact site OPTN forms with ubiquitin and the autophagy machinery provides a more suitable platform for TBK1 autophosphorylation because it maintains TBK1 in a proximal position for a longer period of time.

The OPTN UBAN domain binds a ubiquitin-chain composed of two ubiquitin molecules (Oikawa et al. 2016 Nat Comm), and during Parkin-mediated mitophagy only shorter length poly-ubiquitin chains are generated on the mitochondrial surface (Swatek et al. 2019 Nature). Based on those findings, it is unlikely that multiple OPTN bind to one ubiquitin chain. Of course, we cannot rule out the possibility that TBK1 autophosphorylation does not occur on mitochondria in the absence of autophagy components. While full activation of TBK1 requires OPTN to associate with the isolation membrane, initial TBK autophosphorylation at the onset of mitophagy may occur based only on the OPTN-ubiquitin interaction. These explanations have been added to the Discussion in the revised manuscript.

Furthermore, based on comments from Reviewer 2, we performed time-lapse microscopy to observe OPTN dynamics during Parkin-mediated mitophagy (please see Fig 2l). HeLa cells stably expressing GFP-OPTN and pSu9-mCherry (a mitochondrial marker) were treated with valinomycin. GFP-OPTN was initially a peri- mitochondrial dot-like structure that elongated over time to a cup-shaped structure and which eventually ended up forming a spherical structure. The time-laps imaging showed that, at least in WT cells, OPTN is directly recruited to the contact sites and elongates along with the isolation membranes. We thus concluded that TBK1 is activated (autophosphorylated) at the contact site rather than on the outer membrane where OPTN-TBK can move freely.

• Fig. 5c,d and P. 16: the mitophagy experiments in TBK1-/- cells expressing the different mutant forms of TBK1 are hard to interpret because it is not clear which mitophagy differences are statistically significant. The main text about this part (p. 16) is also confusing.*

We regret the confusion. Reviewer 2 also noted that the main text for Fig 5 was difficult to interpret. One of the reasons that complicated interpretation of the data is the number of TBK1 mutants used. The L693Q and V700Q mutations used by Li et al. (2016 Nat Commun) were expected to inhibit mitophagy since those authors reported that the mutations prevented interactions with OPTN. However, our in-cell assay showed that the two mutants only moderately affected Parkin-mediated mitophagy. Furthermore, both L693Q and V700Q were engineered based on the X-ray structure and are not ALS pathogenic mutations. To simplify the data and to make data interpretation easier, we decided to delete the L693Q and V700A data. We also determined statistical significance and rewrote this section.

• Many graphs lack statistics: Fig. 2b (pTBK1), Fig. 2f, Fig. 5b, Fig. 5d, Fig. 6c.*

We apologize for the lack of statistical analyses. We repeated experiments (if the experiments had not been independently performed more than three times) with statistical significance and error bars incorporated into the relevant figures.

*Other comments: *

• Fig. 1a: how do they know that the upper OPTN band is ubiquitinated OPTN? Reviewer 2 raised the same question. To demonstrate that the upper OPTN band is ubiquitinated, cell lysates after mitophagy induction were incubated in vitro* with a recombinant USP2 core domain, and the samples immunoblotted. As shown in supplementary Fig 1 in the revised manuscript, the upper OPTN band disappeared in a USP2-dependent manner. The upper NDP52 and TOMM20 bands similarly disappeared. Therefore, the upper OPTN, NDP52 and TOMM20 bands observed after mitophagy induction are ubiquitinated.

• Fig. 1a,b: the bafilomycin stabilization of pTBK1, OPTN and pOPTN indicates that these proteins are substantially degraded by autophagy within 30-60 minutes. This seems extremely fast for mitophagy completion. Please discuss.*

According to Kulak et al. (2014 Nat Methods), autophagy adaptor abundance (OPTN: 2.32E+4 and NDP52: 3.34E+4 in HeLa cell line) is low compared to that of mitochondria (TOMM20: 1.45E+6 in HeLa cell line). This is one of the reasons why autophagic degradation of adaptors is easier to see. Degradation of phos-TBK1 was likewise easy to detect, whereas total TBK1 was not. This discrepancy is likely based on differences in the abundance of phos-TBK1 and total TBK1. In addition, because autophagy adaptors are localized outside of the mitochondrial membrane they may be easier targets for lysosomal degradation than matrix proteins, which are localized inside the outer and inner membranes.

• Fig. 1a and rest of the manuscript: is there a reason why the authors only looked at S177 phosphorylation of OPTN and not also at OPTN S473, which is also phosphorylated by TBK1?*

Both mass spectrometry and mutational analyses indicated that OPTN S473 is phosphorylated during Parkin-mediated mitophagy and that OPTN phosphorylated at S473 strongly binds ubiquitin chains (Richter et al. 2016 PNAS and Heo et al. 2015 Mol Cell). However, because a phos-S473 OPTN antibody is, to the best of our knowledge, currently not commercially available, we did not focus on S473 phosphorylation.

• Fig. 1e-f: the main text states that "NDP52 KO effects on the pS172 signal were comparable to controls", but the blot in 1e and the graph in 1f indicate a difference between NDP52KO and WT (significant difference shown in 1f). This is confusing.*

We regret the over-interpretation. As the reviewer indicated, the amount of phos-TBK generated in response to mitophagy was reduced in NDP52 KO cells relative to that in WT cells. This has been corrected. We would like to emphasize that, unlike OPTNdeletion, NDP52 deletion has relatively minor effects on TBK1 phosphorylation.

• P. 9: "TBK1 phosphorylation however was not apparent in the OPTN mutant lines, even after 3 hrs with valinomycin, indicating that autophagy adaptors are essential for TBK1 activation (Fig. 2a)". However, the pTBK1 blot in Fig. 1a does show pTBK1 formation in the OPTN mutant (4LA etc.) lines. This is confusing.*

We apologize for this error. We intended to state “TBK1 phosphorylation was not apparent in the Penta KO cells without OPTN expression even after 3 hrs with valinomycin, indicating that autophagy adaptors are essential for TBK1 activation”. This sentence has been corrected in the revised manuscript.

• P. 10: "we subtracted the basal phosphorylation signal from that generated post-valinomycin (1 hr) and bafilomycin (3 hr)". Do they mean "from that generated post-valinomycin (3 hr) and bafilomycin (3 hr)?*

The reviewer is correct, we have corrected the error.

• P. 10, same paragraph: "the phosphorylation signal was ~90 but was less than 30 in ATG9A KO cells." Unclear what they mean by 90 and 30. 90% and 30%? 90-fold and 30-fold?*

The newly generated pTBK1 levels following Parkin-mediated mitophagy were calculated as pTBK1 [val & baf 3 hrs] minus pTBK1 [DMSO]. Since pTBK1 [val & baf 3 hrs] in WT cells is set to 100%, the newly generated pTBK1 in WT cells was 100% - 5% = 95%. The calculated values for pTBK1 [DMSO] and pTBK1 [val & baf 3 hrs] in ATG9A KO cells were ~55% and ~85%, respectively. Consequently, newly generated pTBK1 in the ATG9A KO cells is ~85% - ~55% = 30%. For clarity, we modified the figure to make the meaning of the numbers more apparent.

• Fig. 3a: Do they have an idea what kind of ubiquitinated substrates are contained in the ubiquitin-positive condensates that accumulate in FIP200 KO and ATG9A KO cells (i.e. without valinomycin treatment)?*

According to Kishi-Itakura et al. (2014 J Cell Sci), ferritin accumulates in the p62 condensates in FIP200 KO and ATG9A KO cells. However, it is unknown if the ferritin in the condensates is ubiquitinated. In the original manuscript, we confirmed by immunostaining that the p62-NBR1 condensates contain ferritin (Fig 3a in the original manuscript and supplementary Fig 7b in the revised manuscript).

• P. 12 and Fig. 3a: please explain why they look at ferritin, to improve readability.*

We thank the reviewer for the suggestion. As mentioned, ferritin is a known substrate that accumulates in p62 condensates, we thus sought to confirm its presence. We have included this explanation in the revised manuscript.

• Fig. 3a: please also include Ub stain for NBR1.*

We thank the reviewer for the suggestion. We obtained a rabbit anti-NBR1 antibody that allowed us to co-immunostain with the mouse anti-ubiquitin antibody (please see supplementary Fig 7b in the revised manuscript).

• Fig. 3d: the OPTN blot shows 2 OPTN bands. What does the upper OPTN band represent here?*

To determine if the two bands are genuine OPTN, total cell lysates prepared from HeLa cells treated with control siRNA or OPTN siRNA were subjected to phos-tag PAGE followed by immunoblotting with an anti-OPTN antibody. As shown below (Figure 2 for reviewers), the two bands (indicated as blue arrowheads) were absent in the OPTN knock down cells, indicating that both are derived from OPTN. Since phosphorylated species migrate slower in phos-tag PAGE, the upper band might be a phosphorylated form. The specific Ser/Thr phosphorylated in OPTN, however, remains to be determined. Heo et al. (2015 Mol Cell) also reported the two OPTN bands on phos-tag PAGE and that both were unchanged in TBK1 KO cells, suggesting that at least the upper band is not affected by TBK1.

• P. 14 and Fig. 4b: "Here, we found that phosphorylation of ... TBK1 (S172) was induced by the OPTN-ub fluoppi (Fig. 4b)." However, Fig 4b does not show a pTBK1 blot.*

We immunoblotted phos-TBK1. Please see Fig 4b in the revised manuscript.

*Reviewer #3 (Significance (Required)): *

*The novel insights are relevant. *

*According to the prevailing model (prior to this manuscript), TBK1 activation via autophosphorylation leads to TBK1-mediated phosphorylation of OPTN S177 and subsequent pOPTN-mediated recruitment of autophagic isolation membranes to the mitochondria. However, based on the model provided in this manuscript, OPTN needs to interact first with both autophagic membranes and ubiquitin before TBK1 can become activated. *

Based on our time-lapse microscopy observations (Fig 2l), OPTN recruited to the vicinity of mitochondria was visible as a small dot-like structures that likely correspond to contact sites between mitochondria and the isolation membrane since OPTN colocalizes with WIPI1 (please see supplementary Fig 2). These results support our proposed model that OPTN interacts with both isolation membranes and ubiquitin at the onset of mitophagy. Without TBK1 activation, OPTN can interact with ATG9A vesicles, a seed for isolation membrane formation (Yamano et al 2020 JCB), and TBK1 can interact with the PI3K complex (Nguyen et al 2023 Mol Cell). Therefore, OPTN-TBK1 can be recruited to the contact site from the very beginning of mitophagy induction prior to TBK1 being fully activated. Furthermore, the proposed model also includes an OPTN-TBK1 positive feedback loop; however, the earliest reactions in the positive feedback loop are too difficult to observe. For example, it’s widely known that PINK1 and Parkin form a positive feedback loop to generate ubiquitin-chains on damaged mitochondria, but the initial reaction has yet to be observed. It remains unclear if PINK1 is the first to phosphorylate mitochondrial ubiquitin (if this is the case, it remains unknown how ubiquitin comes to mitochondria) or if cytosolic Parkin first adds ubiquitin to the outer membrane albeit with very weak activity. Similarly, in our proposed model, we cannot determine the earliest OPTN-TBK1 reaction. As described in the Discussion in the revised manuscript, it remains possible that in the absence of autophagy machinery OPTN distributed freely on the outer membrane can induce trans-autophosphorylation, albeit weakly, as the earliest reaction.

We would like to thank Reviewer 3 for the critical comments and suggestions. We have performed several of the suggested experiments, added new data, and rewritten the text. We hope that these changes have sufficiently addressed the reviewer’s concerns.

Author Response

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

The authors thank the reviewers for their thoughtful and constructive comments. We address each comment below and have uploaded a revised manuscript.

Public Reviews

1) One key point that could use further clarification is how to interpret densities in the reconstruction that do overlap with the template. If the omitted regions can be reliably reconstructed, and the density is smooth throughout, it implies the detected particles are not only (mostly) true positives but also their poses must be essentially correct. Therefore, why cannot the entire reconstruction be trusted, including portions overlapping with the template? In the "Future applications" section, the authors state that in order to obtain a reconstruction that is entirely devoid of template bias, it would be necessary to successively omit parts of the template structure through its entirety. I wonder if that is really necessary and if the presented approach of omitting template portions could be better framed as a "gold-standard" validation procedure.

Our assumption is indeed that the entire reconstruction can be trusted if the omitted features are faithfully reproduced in the reconstruction. We have added a sentence in the discussion to clarify this. However, we think that assessing template bias will still require the omit test (see also our reply below). Also, as discussed in the manuscript, there is likely a little bias left, even if it is not directly visible in the reconstruction. Therefore, if the goal is an entirely unbiased reconstruction, the only way will be to successively omit parts of the template structure throughout the template.

2) In other words, given the compelling evidence provided by the reconstructions in the omitted areas, I find it hard to imagine how the procedure would be "hallucinating" features in the rest of the structure, as the entire reconstruction depends on the same pose and defocus parameters. A possible experiment to test this hypothesis would be to go the opposite way, deliberately adding an unrealistic feature to the bait and checking whether it comes up in the reconstruction, while at the same time checking how it behaves in omitted parts.

Template bias might be generated in different ways. A common situation is the presence of noise, which causes biased deviations of the best template match from their “true” match that would just align the target signal to the template. Another type of bias may occur when there is a mismatch between the template and the detected target. The target may still be detected if there is sufficient structural overlap with the template. Since there might not be a clear “correct” alignment of a mismatching target to the template, the best alignment may again be biased, generating artificial density in the reconstruction. This second case may produce bias that is more pronounced in the mismatching regions. The different origins of bias will have to be investigated more thoroughly in another study. For the present study, however, we maintain that unless there is some assessment of bias in a given location, one cannot completely rule out bias based on the absence of it elsewhere in the reconstruction.

3) When assessing their approach to in situ data (the yeast ribosome), it is intriguing to see that the resolution downgraded from 3.1 to 8 Å when refinement of the particle poses against the current reconstruction was attempted. The authors do provide some possible explanations, such as the reduced signal of the reconstruction at high resolution and the crowded background, but it leaves one to wonder if this means that a 3.1 Å reconstruction could never be obtained from these data by conventional single-particle analysis procedures.

The refinement results with our in situ data do indeed appear to be limited to low resolution when using the conventional single-particle pipeline and software. It might be possible to improve refinement by introducing certain priors, filters and masking functions that are optimized for the increased background and spectral properties of in situ data. Also, we have not tested all available software, and some might perform better than others. It is worth noting that in a different study using our data, by Cheng et al (2023) and cited in our manuscript, the resolution of the refined reconstruction using different software was ~7 Å resolution, i.e., close to what we report here. Finally, refinement of the detected targets against a high-resolution template does work but since it involved the template, we regard this as part of the template matching process.

4) Furthermore, in the section "Quantifying template bias", the authors make the intriguing statement that there can still be some overfitting of noise even in true positives. I understand this overfitting would occur in the form of errors in the pose and defocus estimation, but a clarification would be helpful.

We have added a sentence in the Discussion to clarify where this bias may come from.

5) In the Discussion, the claim that "it is not necessary to use tomography to generate high-resolution reconstructions of macromolecular complexes in cells" is a misconception, at least in part. As demonstrated in works by the same group and others (https://doi.org/10.1016/j.xinn.2021.100166, https://doi.org/10.1038/s41467-023-36175-y, https://doi.org/10.1038/s41586-023-05831-0), 2D imaging of native cellular environments does offer a faster and better way to obtain high-resolution reconstructions compared to tomography. However, tomography provides the entire 3D context of the macromolecules, such as their localization to membranes and the cellular architecture, which can be readily visualized in a tomogram even at low resolution, so methods for structure determination from tilt series data such as subtomogram averaging remain of paramount importance. Most likely, a combination of 2D and 3D imaging approaches will be necessary to retrieve both the highest structural resolution and their cellular context to address biological questions.

We agree and have modified our statement accordingly.

6) The "Materials and Methods" section lacks a description of transmission electron microscopy data collection.

We are sorry for this oversight and have added these details.

7) Finally, the preprint version of this work posted on bioRxiv (https://doi.org/10.1101/2023.07.03.547552) contains the following competing interests statement, which is missing from the submitted version: "The authors are listed as inventors on a closely related patent application named "Methods and Systems for Imaging Interactions Between Particles and Fragments", filed on behalf of the University of Massachusetts."

This is correct. The statement was missing in the first version of the uploaded manuscript and was added after consultation with the eLife editorial office.

8) Quantification of the amount of model bias is then performed using omit maps, where every 20th residue is removed from the template and corresponding reconstructions are compared (for those residues) with the full-template reconstructions. As expected, model bias increases with lower thresholds for the picking. Some model bias (Omega=8%) remains even for very high thresholds. The authors state this may be due to overfitting of noise when template-matching true particles, instead of introducing false positives. Probably, that still represents some sort of problem. Especially because the authors then go on to show that their expectation of the number of false positives does not always match the correct number of false positives, probably due to inaccuracies in the noise model for more complicated images. This may warrant further in-depth discussion in a revised manuscript.

We have added further thoughts regarding the mismatch between expected and actual number of false positives in the Discussion section. A full understanding of the issue likely requires further study, which is currently underway.

9) The authors evaluate the effect of high-resolution 2D template matching on template bias in reconstructions, and provide a quantitative metric for overfitting. It is an interesting manuscript that made me reevaluate and correct some mistakes in my understanding of overfitting and template bias, and I'm sure it will be of great use to others in the field. However, its main point is to promote high-resolution 2D template matching (2DTM) as a more universal analysis method for in vitro and, more importantly, in situ data. While the experiments performed to that end are sound and well-executed in principle, I fail to make that specific conclusion from their results.

We do not see 2DTM as a more universal analysis method for in vitro and in situ data, but as simply as another method that can be used. We have added a sentence in the introduction to clarify this.

10) The authors correctly point out that overfitting is largely enabled by the presence of false-positives in the data set. They go on to perform their in situ experiments with ribosomes, which provide an extremely favorable amount of signal that is unrealistic for the vast majority of the proteome. This seems cherry-picked to keep the number of false-positives and false-negatives low. The relationship between overfitting/false-positive rate and the picking threshold will remain the same for smaller proteins (which is a very useful piece of knowledge from this study). However, the false-negative rate will increase a lot compared to ribosomes if the same high picking threshold is maintained. This will limit the applicability of 2DTM, especially for less-abundant proteins.

The reviewer is correct that the lower SNR of smaller targets poses a fundamental limit to 2DTM. We have stated this in previous studies and have added a sentence in the introduction of the current manuscript to clarify this.

11) I would like to see an ablation study: Take significantly smaller segments of the ribosome (for which the authors already have particle positions from full-template matching, which are reasonably close to the ground-truth), e.g. 50 kDa, 100 kDa, 200 kDa etc., and calculate the false-negative rate for the same picking threshold. If the resulting number of particles does plummet, it would be very helpful to discuss how that affects the utility of 2DTM for non-ribosomes in situ.

The suggested ablation study is a good idea and was reported by Rickgauer et al (2020), cited in our manuscript. We added our own analysis for this dataset in Figure 4-figure supplement 1 and show the proportion of LSUs detected as a function of template mass, indicating detection limit of ~300 kDa. We also added a note in the Results section to explain that the threshold we use to limit false positives means that there are also false negatives, with a rate that depends on their molecular mass.

12) Another point of concern is the dramatic resolution decrease to 8 A after multiple iterations of refinement against experimental reconstructions described in line 159. Was this a local search from the poses provided by 2DTM, or something more global? While this is not a manifestation of overfitting as the authors have conclusively shown, I think it adds an important point to the ongoing "But do we really need tomograms, or can we just 2D everything?" debate in the field, which is also central to the 2D part of 2DTM. Reaching 8 A with 12k ribosome particles would be considered a rather poor subtomogram averaging result these days. Being in the "we need tilt series to be less affected by non-Gaussian noise" camp myself, I wonder if this indicates 2D images are inherently worse for in situ samples. If they are, the same limitations would extend to template matching. In that case, shouldn't the authors advocate for 3DTM instead of 2DTM? It may not be needed for ribosomes, but could give smaller proteins the necessary edge.

We have extensively discussed the advantages and disadvantages of both tomography and 2DTM (Lucas et al, 2021) and think it is not useful to talk in terms of “better” and “worse”. Instead, each technique has its areas of application, and we maintain that a combination of the two may give the best results. The limitation of 8 Å does not apply to reconstructions aligned against high-resolution templates, as demonstrated in the present study. Regarding noise models, there is also need for these in 3DTM, as explained in recent publications: Maurer et al (2023), bioRxiv, doi.org/10.1101/2023.09.06.556487; Cruz-León et al (2023), bioRxiv, doi.org/10.1101/2023.09.05.556310; Chaillet et al (2023), Int. J. Mol. Sci. 24, 13375.

13) Right now, this study is also an invitation to practitioners who do not understand the picking threshold used here and cannot relate it to other template-matching programs to do a lot of questionable template matching and claim that the results are true because templates are "unoverfittable". I think such undesirable consequences should be discussed prominently.

We have added a discussion of this point in the Discussion section.

Recommendations for the authors

1) Lines 58-59: What does "nominally untilted" mean? Has the lamella pre-tilt (milling angle) been taken into account or not? If yes, how?

The lamella milling angle was not taken into account, so there is a tilt built into the sample of about 8° that was not compensated for by a counter-tilt of the microscope goniometer. We have added a note to explain this in the text of the manuscript.

2) Lines 113-114: A brief explanation of the threshold calculation method from Rickgauer et al, 2017 to achieve an expected false positive rate of one per micrograph would be helpful here.

We describe the equation for estimating the false discovery rate later in the manuscript. We have added a note in the text to point the reader to the relevant section of the manuscript.

3) For consistency, it would be interesting to include a plot of the SNR peaks found by 2DTM in the in situ dataset, that could be directly compared to Figure 1 - figure supplement 1B.

We have added this to Figure 2 - figure supplement 1A-C, to directly compare to Figure 1 – figure supplement 1A-C.

4) Showing model-map FSC curves between the density retrieved from the omitted areas and their respective models would provide further evidence not only that they are correct but to what extent.

An FSC calculation would be challenging for small regions, such as side chains and drugs, due to masking artifacts. Moreover, the model was built into an in vitro determined map and was not fit into the in vivo map calculated here. Therefore, deviations between the map and model may reflect differences between the two conditions and may not reflect the agreement of the map to the in vivo structure.

5) Lines 128-130: The figure references are wrong. Here, Figure 1B should probably be Figure 1A (or 1B), and Figure 1C clearly refers to Supplementary Figure 1F (FSC curve).

We have corrected the incorrect figure references.

6) Line 125: Wrong figure reference, Figure 1A here refers to Supplementary Figure 1B (cross-correlation peaks).

We have corrected the incorrect figure references.

7) I haven't been able to find mention of code availability in the manuscript. Given that it is a major outcome of the study, I think it should be provided.

The code is available from the cisTEM repository, github.com/timothygrant80/cisTEM, and an executable version of the program measure_template_bias has been posted for download on the cisTEM webpage, cistem.org. We have added a note in the Methods section to point the readers to these resources.

8) Line 50: "An additional complication of subtomogram averaging for in situ imaging is the selection of valid targets" - This is not specific to subtomogram averaging, but to in situ samples.

We agree and have updated the text to reflect this.

9) Line 77: "if this is true for high-resolution features, which are more susceptible to noise overfitting" - This is not intuitive to me. High-resolution features require more information to be overfitted with a constant set of model parameters, thus making their overfitting harder.

The reviewer is correct that there is more information at high resolution, partially compensating for the low SNR. However, the overall refinement behavior is still dominated by overfitting at high resolution, as we have demonstrated in an earlier publication in Stewart & Grigorieff (2004), Ultramicroscopy 102, 67–84.

10) Line 316: "Baited reconstruction is substantially faster and a more streamlined" - To back this and other similar statements, it would be helpful if the authors provided some time measurements for the execution of their potentially very computationally expensive search.

The current implementation of 2DTM requires 45 GPU hours per template per K3 image to search 13 defocus planes. However, for a comparison, the manual work for annotation, as well as additional processing to align and classify sub-tomograms to generate high resolution averages should also be considered in this comparison. These are highly project-dependent and can exceed the time required for 3DTM manifold. We have clarified this in our Discussion section.

11) Line 319: "We expect focused classification to identify sub-populations to further improve the resolution" - How would this work if refining the 2D data without a high-resolution template resulted in significantly worse resolution even for a ribosome? Or is this meant to be done with prior knowledge of every state?

Classification can be done using existing single particle software. To avoid alignment errors, as described above, particle alignment angles and shifts are fixed during classification. This leaves only the particle occupancy per class to be refined, which appears to lead to good classification. We have added a brief note to explain this strategy. However, since this is not shown in this manuscript, we have not added a more extensive discussion of particle classification.

12) Line 354: "without requiring manual intervention or expert knowledge" - Previous expert knowledge was arguably provided in the form of a high-resolution structure.

We agree with the reviewer and have clarified our statement.

I think this is an interesting point she states as it's a viewpoint I've upheld before. Viewing social media vs the real world in a black and white matter may do more harm than good as in today's world not going on social media is the equivalent of social isolation. Yet having to go on social media and scrolling aimlessly and endlessly will also overstimulate and lead to negative emotions. Rather than either hopping on or off for extended periods of time, I think regulation is key, both with the way in which we scroll and how much.

It is true and I have similar experience. When I spent time, browsing the social media platforms, the time is extremely "faster" as I imagine. It is also the reason why some people spend "their whole life" on internet. I think to reasonably balance our leisure time and work/study, we should set the time for entertaining at first and stop to study/work at that settled time.

Author Response

Reviewer #1:

We thank Reviewer #1 for their review of our manuscript.

Reviewer #1, comment #1: “The authors of this manuscript are from the Canadian, public interest open-science company YCharos.”.

It is important to state that none of the authors work for YCharOS. The YCharOS company has created an open ecosystem consisting of antibody manufacturers, knockout cell lines providers, academics, granting agencies and publishers. The Antibody Characterization Group (participating authors are affiliated to the Department of Neurology and Neurosurgery, Structural Genomics Consortium, The Montreal Neurological Institute, McGill University) works in collaboration with YCharOS to have access to commercial antibodies and knockout cell lines donated by YCharOS’ manufacturer partners.

Reviewer #1, comment #2: In regard to ZENODO antibody characterization reports prepared by this group, Reviewer #1 wrote: “While the results are convincing, they could be more accessible. In the current format, researchers have to download reports for each target and look through all images to identify the most useful antibodies from the images. The reports I reviewed did not draw conclusions on performance. A searchable database that returns validated antibodies for each application seems necessary.”

After careful consideration and consultation with YCharOS industry partners, we decided not to rate the performance of the antibodies tested. It was determined that antibody selection is best left to the user, who should analyze all parameters, including the type of antibody to be chosen (recombinant-monoclonal, recombinant-polyclonal, monoclonal), the species used to generate the antibody, the species predicted to react with the antibody, performance in a specific application, antigen sequences, and antibody cost.

Reviewer #1, comment #3: “A key question is to what extent off-target binding was predictable from the WBs provided by the manufacturers. Thus, how often did the authors find multiple bands when the catalogue image showed a single band and vice versa?”

In many cases, the antibodies were tested on cell lines other than those used by the manufacturers. Given that protein expression is specific to each line, we can't answer this question properly.

Reviewer #1, comment #4: “Cross-reactive proteins will generally not be detected when blots are stained with an antibody reactive with a different epitope than the one used for IP. Possible solutions to overcome this limitation such as the use of mass spectrometry as readout should be discussed (Nature Methods volume 12, pages 725- 731 (2015)”.

Our protocols only inform whether an antibody can capture the intended target, without any evaluation of the extend to the capture of unwanted, cross-reactive proteins. Thus, our data can only be used to aid in selection of the best performing antibodies for IP – our data does not inform profiling of non-specific interactions.

IP/mass spec is an excellent approach for evaluating antibody performance for IP, and authors on this manuscript are experts in proteomics and recognize the importance of this methodology. We have considered implementing IP/mass in our platform. However, there are limitations, such as the cost of the approach and the difficulty of detecting smaller proteins or proteins with a certain amino acid composition (high presence of Cys, Arg or Lys). Fundamentally, we have decided to focus on throughput relative to details in this regard.

Reviewer #1, comment #5: “Performance in immunofluorescence microscopy was performed on cells that were fixed in 4% paraformaldehyde and then permeabilized with 0.1% Triton-X100. It seems reasonable to assume that this treatment mainly yields folded proteins wherein some epitopes are masked due to cross-linking. The expectation is therefore that results from IP are more predictive for on-target binding in IF than are WB results (Nature Methods volume 12, pages725-731 (2015). It is therefore surprising that IP and WB were found to have similar predictive value for performance in IF (supplemental Fig. 3). It would be useful to know if failure in IF was defined as lack of signal, lack of specificity (i.e. off-target binding) or both. Again, it is important to note the IP/western protocol used here does not test for specificity.”

The assessment of antibody performance is biased by how antibodies were originally tested by suppliers. Manufacturers primarily validate their antibody by WB. Thus, most antibodies immunodetect their intended target for WB. Thus, in retrospect, we tested a biased pool of antibodies that detect linear epitopes. Still, we observed that a large cohort of antibodies show specificity for their target across all three applications or for specific combinations of applications. This slightly challenges the idea that antibodies are fit-for-purpose reagents and can recognize either linear or native epitopes - a significant number of antibodies can specifically detect both types of epitope.

Reviewer #1, comment #6: “The authors report that recombinant antibodies perform better than standard monoclonals/mAbs or polyclonal antibodies. Again, a key question is to what extent this was predictable from the validation data provided by the manufacturers. It seems possible that the recombinant antibodies submitted by the manufacturers had undergone more extensive validation than standard mAbs and polyclonals”.

Our antibody manufacturing partners indicated that the recombinant antibodies are more recent products and have been more extensively characterized relative to standard polyclonal or monoclonal antibodies.

The main message is that recombinant antibodies can be used in all applications once validated. Although recombinant antibodies are available for many proteins, the scientific community is not adopting these renewable regents as we believe it should. We hope that the data provided will encourage scientists to adopt recombinant technologies when available to improve research reproducibility.

Reviewer #1, comment #7: “Overall, the manuscript describes a landmark effort for systematic validation of research antibodies. The results are of great importance for the very large number of researchers who use antibodies in their research. The main limitations are the high cost and low throughput. While thorough testing of 614 antibodies is impressive and important, the feasibility of testing hundreds of thousands of antibodies on the market should be discussed in more detail.”

We thank the reviewer for this comment. One of our challenges is to increase the platform's throughput to succeed in our mission to characterize antibodies for all human gene products. We will continue to test antibodies using protocols agreed upon with our partners, commonly used in the laboratory, to ensure that ZENODO reports can serve as a guide to the wider community.

In terms of development our marketing efforts have been substantially accelerated by our new partnership with the journal F1000. We have begun to convert our reports into peer-reviewed papers (20 ZENODO reports were converted into F1000 articles). This conversion allows researchers to find our work via PubMed, and easily cite any study. Producing peer-reviewed articles also further enhances the credibility of our research and our project as a whole: https://f1000research.com/ycharos

Colleagues have published a letter to Nature explaining the problem and our technology platform: (Kahn, et al., Nature, 2023, DOI: https://doi.org/10.1038/d41586-023-02566-w).

This project has been presented worldwide, with a presence at major antibody conferences, such as the annual Antibody Validation meeting in Bath (PSM attended the meeting in September 2023). The authors are organizing a sponsored mini-symposium on antibody validation at the next American Society for Cell Biology (ASCB) meeting in December 2023 (Boston, USA): https://plan.core- apps.com/ascbembo2023/event/6fb928f06b0d672e088c6fa88e4d77fb

Colleagues have prepared petitions addressed to various governmental organizations (US, Canada, UK) to support characterization and validation of renewable antibodies: https://www.thesgc.org/news/support- characterization-and-validation-renewable-antibodies.

Reviewer #2

We thank Reviewer #2 for the review of the antibody characterization reports we have uploaded to ZENODO. A manuscript describing the full standard operating procedures of the platform, which has been used in all reports is in preparation, and should be available on a preprint server before the end of the year. Our protocols were reviewed and approved by each of YCharOS' manufacturer partners. Moreover, a recent editorial describes the platform used here and gives advice on how to interpret the data: https://doi.org/10.12688/f1000research.141719.1)

Reviewer #2, comment #1: “A discussion of how the working concentrations of antibodies are selected and validated is required. Based on the dilutions described in the reports, it seems that dilutions suggested by the manufacturer were used - For LRRK2 it seems that antibody concentrations ranging from 0.06 to over 5 µg/ml for WB were used. Often commercial antibody comes in a BSA-containing buffer making it hard to validate the concentration of the antibody claimed by the manufacturer”.

The concentration recommended by the manufacturer is our starting point. For WB, when the signal is at the level of detectability, we will repeat with a ~5-10 fold increase in antibody concentration. For >80% of the antibody tested, the use of the recommended concentration led to the detection of bands (specific or not to the target protein).

Reviewer #2, comment #2: “In the authors' experience are the manufacturer's concentrations reliable? Additionally, if the information regarding applications provided by the manufacturers is unreliable how do the authors suggest working concentrations for antibodies to be assessed”?

We do not evaluate the concentration of antibodies internally. In the immunoprecipitation experiments, we use 2.0 µg of antibody for each IP, based on the concentration provided by the manufacturers. On Ponceau staining of membranes, we can observe the heavy and light chains of the primary antibodies used, giving an indication of the amount of antibodies added to the cell lysate. In most cases, the intensity of the heavy and light chains is comparable.

Reviewer #2, comment #3: “We understand that it would not be feasible to test every antibody at different concentrations, but this is an issue that should at least be mentioned. An antibody might be put in the wrong performance category solely because of the wrong concentration being used. Ie if an excellent antibody is used at too high a concentration, it may detect non-specific proteins that are not seen at lower dilutions where the antibody still picks up the desired antigen well”.

We agree with Reviewer #2, we do not use an optimal concentration for all tested antibodies. As mentioned previously, the concentration recommended by the manufacturer is our starting point. By testing multiple antibodies side-by-side against a single target protein, we can generally identify one or more specific and selective antibodies. We leave it to users of our reports to optimize the antibody concentration to suit their experimental needs.

Reviewer #2, comment #4: “Do the authors check different WB conditions ie 2h primary antibody with BSA or milk vs. overnight at 4 degrees with BSA or Milk”?

All primary antibodies are always tested in milk overnight at 4 degrees. The overnight incubation is convenient in the timeline of the protocol. All protocols were agreed upon after careful consultation with our partners.

Reviewer #2, comment #5: “Do the authors provide detailed WB protocols that include the description of the electrophoresis and type of gels used, transfer buffer and transfer method and time used, and conditions for all the primary and secondary blotting including times, buffers and dilutions of all antibodies and other reagents”?

This information is included in all ZENODO reports.

Reviewer #2, comment #6: “Do the authors discuss detection approaches- we have noticed for some antibodies there are significant different results using LICOR, ECL and other detection methods, with certain especially weaker antibodies preferring ECL-based methods”.

We only use ECL-based methods.

Reviewer #2, comment #7: “For IPs the amount of antibody needed can also vary-for some we can use 1 microgram or less, but for others, we need 5 to 10 micrograms. The amount of antibody needed to get maximal IP should be stated”.

We use 2.0 ug of antibodies and we have found this to be adequate for lower abundance proteins (e.g. Parkin - https://zenodo.org/records/5747356) and higher abundance proteins (e.g. PRDX6 - https://zenodo.org/records/4730953). Abundance is based on PaxDb.com. For Parkin and PRDX6, we were able to enrich the expected target in the IP and observe depletion in the unbound fraction. Optimization of the IP conditions is left to the antibody users.

Reviewer #2, comment #8: “Doing IPs with commercial antibodies can be very expensive or infeasible if many micrograms are needed especially if only packages of 10 micrograms for several hundred dollars are provided”.

This is a major advantage of the side-by-side comparison: the reader is free to choose between high-performance antibodies from different manufacturers, with varying antibody costs. We also work in partnership with the Developmental Studies Hybridoma Band (DSHB), which supplies antibodies on a cost recovery basis.

Reviewer #2, comment #9: “For IPs it is important to determine the percentage of antigen that is depleted from the supernatant for each IP. We think that this should be calculated and recorded in the Zenodo data. Some antibodies will only IP 10% of antigen whereas others may do 50% and others 80-90%. One rarely sees 100% depletion. For IPs the buffer detergent and salt concentration might also strongly influence the degree of IP and therefore these should be clearly stated”.

In Box 1, we define criteria of success. For IP, “under the conditions used, a successful primary antibody immunocaptures the target protein to at least 10% of the starting material”. Colleagues have written an editorial on how to interpret and analyze antibody performance https://f1000research.com/articles/12-1344).

The cell lysis buffer is a critical reagent when considering IP experiments. We use a commercial buffer consisting of 25 mM Tris-HCl pH 7.4, 150 mM NaCl, 1 mM EDTA, 1% NP-40 and 5% glycerol (Thermo Fisher, cat. #87787). This buffer is efficient to extract the target proteins we have studied thus far.

Reviewer #2, comment #10: “Whether antibodies cross-react with human, mouse and other species of antigens is always a major question. It is always good to test human and mouse cell lines if possible. If antibodies cross-react in WB, in the authors' experience will they also cross-react for IF and IP”?

The authors started this initiative by focusing on the 20,000 human proteins, defining an end point. We and our collaborators found that most of the cherry-picked selective antibodies for WB for human proteins, which manufacturers claim react with the murine version of the target proteins, were selective for murine tissue lysates.

Indeed, poorly performing antibodies in WB mostly failed IF and IP. However, selective antibodies for IF or specific for IP were generally (>90%) selective for WB.

Reviewer #2, comment #11: “Cell lines express proteins at vastly different levels and it is possible that the selected cell line does not express the antigen or expresses it at very low levels - this could be a reason for wrongly assessing an antibody not working. It would be useful to use cell lines in which MS data has defined the copy number of protein per cell and this figure could be included in the antibody data if available. This MS data is available for the vast majority of commonly used cells”.

We agree with Reviewer #2 that MS data are useful for target protein selection. At the moment, our approach using transcriptomic data provided on DepMap.org proved to be a successful mechanism for cell line selection. We have identified a specific antibody for WB for each target, enabling the validation of expression in the cell line selected.

For some protein targets, the parental line corresponding to the only commercial or academic knockout line available has weak protein expression. We thus needed to generate a KO clone in a second cell line background with high expression, and indeed found that some antibodies which failed in the first commercial line were successful in the new higher-expressing line (e.g CHCHD10 - https://zenodo.org/records/5259992).

Reviewer #2, comment #12: “Some proteins are glycosylated, ubiquitylated or degraded rapidly making them hard to see in WB analysis”.

We used the full gel/membrane length when analyzing antibody performance by WB. Indeed, proteins can show different isoforms and molecular weights compared to that based on amino acid sequence (e.g. SLC19A1 -https://zenodo.org/records/7324605).

Reviewer #2, comment # 13: “We have occasionally had proteins that appear unstable when heated with SDS- sample buffer before WB. For these, we still use SDS-Sample buffer but omit the heating step. I often wonder how necessary the heating step is”.

For WB, samples are heated to 65 degrees, then spun to remove any precipitate.

Reviewer #2, comment # 14: “For IF the methods by which cells are fixed and stained, and the microscope and settings, can significantly influence the final result. It would be important to carefully record all the methods and the microscope used”.

We agree with Reviewer #2 that many parameters influence antibody performance for imaging purposes. We are progressively implementing the OMERO software to monitor any experimental parameters and information (metadata) about the microscope itself.

Reviewer #2, comment # 15: “How do the authors recommend antibodies are stored? These should be very stable, but I have had reports from the lab that some antibodies become less good when stored and others that recommend storing at 4 degrees”.

Antibodies are aliquoted to avoid freeze-thaw cycles and stored at -20 degrees. If it is recommended to store antibodies at 4 degrees, we add glycerol to a final concentration of 50% and store them at -20 degrees.

Reviewer #2, comment # 16: “Would other researchers not part of the authors' team, be able to add their own data to this database validating or de-validating antibodies? This would rapidly increase the number of antibodies for which useful data would be available for. It would be nice to greatly expand the number of antibodies being used in research and this is not feasible for a single team to undertake”.

Yes! We believe that only a community effort can resolve the antibody liability crisis. We partner with the Antibody Registry (antibodyregistry.org - led by co-author Anita Bandrowski). In the Registry, each antibody is labelled with a unique identifier, and third-party validation information can be easily tagged to any antibody. Antibody users are invited to upload information about an antibody they have characterized into the Registry.

Author Response

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

We were pleased with seeing our work published as a Reviewed Preprint online so swiftly. Now, we would like to take the opportunity to include our responses to the comments made by the reviewers into the Reviewed Preprint and also submit a revised version of the manuscript, in which we have incorporated and addressed the reviewers’ comments.

We believe that our revisions have significantly improved the quality of the manuscript. Specifically, we have described our results more precisely and explained certain decisions that were made in the analysis pipeline more clearly. For example, Figure 4 was improved substantially, by incorporating a schematic representation of how ERP traces were extracted from neural data. Furthermore, we have added three paragraphs in the Discussion where we elaborate on 1) the two observed interaction effects between attention and drug condition, 2) the relation between behavioral, computational, and neural effects, and 3) the statistical robustness of our findings. As such, we believe our interpretation of the results and their robustness now more faithfully represents our observations.

Moreover, we have incorporated the Supplementary Information and Figures, initially presented as a separate section of the manuscript, to the main manuscript and its accompanying supplementary figures. Thereby, the structure of the paper now better follows the eLife format. As a result, some of the previously included supplementary figures are now described in text of the main manuscript.

Reviewer #1 comments:

In the results section on page 6, the authors conclude that "Attention and ATX both enhanced the rate of evidence accumulation towards a decision threshold, whereas cholinergic effects were negligible." I believe "negligible" is wrong here: the corresponding effects of donepezil had p-values of .09 (effect of donepezil on drift rate), .07 (effect of donepezil on the cue validity effect on drift rate) and .09 (effect of donepezil on non-decision time), and were all in the same direction as the effects of atomoxetine, and would presumably have been significant with a somewhat larger sample size. I would say the effects of donepezil were "in the same direction but less robust" (or at the very least "less robust") instead of "negligible".

We agree with the reviewer that ‘negligible’ may not properly capture the effects of DNP on DDM parameter estimates. Although we do feel that caution is warranted in interpreting the effects of DNP on computational parameter estimates, we have now described these effects in line with the reviewer’s suggestion: in the same direction as the effects of ATX, but not (or less) statistically robust.

"In the results section on page 8, the authors conclude that "Summarizing, we show that drug condition and cue validity both affect the CPP, but they do so by affecting different features of this component (i.e. peak amplitude and slope, respectively)." This conclusion is a bit problematic for two reasons. First, drug condition had a significant effect not only on peak amplitude but also on slope. Second, cue validity had a significant effect not only on slope but also on peak amplitude. It may well be that some effects were more significant than others, but I think this does not warrant the authors' conclusion.

Indeed, we observed that cue validity affected both CPP peak amplitude and slope and some effects were more significant than others. As such, we agree with the reviewer that the conclusion that cue validity and drug condition affect different features of the CPP was too strongly formulated. We have changed this statement in the manuscript to reflect the observed data pattern more appropriately. We would however like to point out that this does not undermine our main conclusion. Spatial attention and drug condition showed only limited interaction effects in terms of behavior and neural data and their effects on occipital activity were separable in terms of timing and spatial profile. Therefore, our conclusion that catecholamines and spatial attention jointly shape perceptual decision-making remains valid.

In the discussion section on page 11, the authors conclude that "First, although both attention and catecholaminergic enhancement affected centro-parietal decision signals in the EEG related to evidence accumulation (O'Connell et al., 2012; Twomey et al., 2015), attention mainly affected the build-up rate (slope) whereas ATX increased the amplitude of the CPP component (Figure 3D-F)." As I wrote above, I believe it is not correct that "attention mainly affected the build-up rate or slope", given that the effect of cue-validity on CPP slope was also significant. Also, while the authors' data do support the conclusion that ATX increased the amplitude and not the slope of the CPP component, a previous study in humans found the opposite: ATX increased the slope but did not affect the peak amplitude of the CPP (Loughnane et al 2019, JoCN, https://pubmed.ncbi.nlm.nih.gov/30883291). Although the authors cite this study (as from 2018 instead of 2019), they do not draw attention to this important discrepancy between the two studies. I encourage the authors to dedicate some discussion to these conflicting findings.

We thank the reviewer for spotting this error, we cited the preprint version (from 2018) of Loughnane and colleagues and not the published JoCN paper (from 2019). We have changed this in the updated version of the manuscript. We further thank the reviewer for asking about this interesting discrepancy between our observation that ATX increased CPP peak amplitude in absence of slope effects and the observation by Loughnane et al. (2019, JoCN) that ATX increased CPP slope, but not amplitude. We first would like to point out that the peak amplitude effect in Loughnane et al. (2019) was in the same direction as our reported effect, with numerically higher peak amplitudes for ATX compared to PLC (Figure 2A – right panel in Loughnane et al., 2019). However, as their omnibus main effect of drug condition on CPP peak amplitude was not significant, they did not provide statistics for a pairwise comparison of ATX and PLC in terms of CPP peak amplitude, which makes it hard to compare the effects directly. Regardless, Loughnane et al. (2019) did observe an effect on CPP slope, whereas we did not. Speculatively, this difference could be related to the behavioral tasks that were used in both studies. Below we have added a new paragraph from the Discussion in which we elaborate on this more.

In Discussion, page 15:

Here, we demonstrated that response accuracy and response speed are differentially represented in the CPP, with correct vs. erroneous responses resulting in a higher slope and peak amplitude, whereas fast vs. slow responses are only associated with increased slopes (Figure 3A-B). Speculatively, the specific effect of any (pharmacological) manipulation on the CPP may depend on task-setting. For example, Loughnane et al. (2019) used a visual task on which participants did not make many errors (hit rate>98%, no false alarms), whereas we applied a task in which participants regularly made errors (roughly 25% of all trials). Possibly, the effects of ATX from Loughnane et al. (2019) in terms of behavior (RT effect, not accuracy/d’) and CPP feature (slope effect, not peak) may therefore have been different from the effects of ATX we observed on behavior (d’ effect, not RT) and CPP feature (peak effect, not slope). Regardless, when we compared subjects with high and low drift rates (Figure 3C), we observed that both CPP slope and CPP peak were increased for the high vs. low drift group (independent of the drug or attentional manipulation). This indicates that both CPP slope and CPP peak were associated with drift rate from the DDM. Clearly, more work is needed to fully understand how evidence accumulation unfolds in neural systems, which could consequently inform future behavioral models of evidence accumulation as well.

On page 12 and page 14 the authors suggest a selective effect of ATX on tonic catecholamine activity, but to my knowledge the exact effects of ATX on phasic vs. tonic catecholamine activity are unknown. Although microdialysis studies have shown that a single dose of atomoxetine increases catecholamine concentrations in rodents, it is unknown whether this reflects an increase in tonic and/or phasic activity, due to the limited temporal resolution of microanalysis. Thus, atomoxetine may affect tonic and/or phasic catecholamine activity, and which of these two effects dominates is still unknown, I think.

We agree with the reviewer that the direct effects of ATX on tonic versus phasic catecholaminergic activity are not clear as initially stated in the manuscript. Equally problematic, previous work has demonstrated that changes in tonic neuromodulation shape evoked neuromodulatory discharge (Aston-Jones & Cohen, 2005, Annu. Rev. Neurosci; Knapen et al., 2016, PLoS ONE). As such, any effect of ATX on tonic neuromodulatory drive would probably have affected phasic catecholaminergic responses as well, although this claim will have to be experimentally addressed. We think that because of the close relation between tonic and phasic neuromodulation, it may indeed be better to refrain from the simplistic interpretation that ATX (and DNP) solely and specifically affects tonic neuromodulation. We have used more neutral language in that regard in the updated version of the manuscript, for example by only mentioning elevated neuromodulator levels (not specifying tonic or phasic). Moreover, we have extended a part of our previous Discussion, to elaborate this issue in more detail. An excerpt of this paragraph, consisting of previous and newly added text, can be seen below.

In Discussion, page 14:

In contrast with recent work associating catecholaminergic and cholinergic activity with attention by virtue of modulating prestimulus alpha-power shifts (Bauer et al., 2012; Dahl et al., 2020, 2022) and attentional cue-locked gamma-power (Bauer et al., 2012; Howe et al., 2017), the current work shows that the effects of neuromodulator activity are relatively global and non-specific, whereas the effects of spatial attention are more specific to certain locations in space. Our findings are, however, not necessarily at odds with these previous studies. Most recent work associates phasic (event-related) arousal with selective attention (for reviews see: Dahl et al., 2022; Thiele & Bellgrove, 2018). For example, cue detection in visual tasks is known to be related to cholinergic transients occurring after cue onset (Howe et al., 2017; Parikh et al., 2007). Contrarily, in our work we aimed to investigate the effects of increased baseline levels of neuromodulation by suppressing the reuptake of catecholamines and the breakdown of acetylcholine throughout cortex and subcortical structures. Tonic and phasic neuromodulation have previously been shown to differentially modulate behavior and neural activity (de Gee et al., 2014, 2020, 2021; McGinley et al., 2015; McGinley, Vinck, et al., 2015; van Kempen et al., 2019). Note, however, that it is difficult to investigate causal effects of tonic neuromodulation in isolation of changes in phasic neuromodulation, mostly because phasic and tonic activity are thought to be anti-correlated, with lower phasic responses following high baseline activity and vice versa (Aston- Jones & Cohen, 2005; de Gee et al., 2020; Knapen et al., 2016). As such, pharmacologically elevating tonic neuromodulator levels may have resulted in changes in phasic neuromodulatory responses as well. Concurrent and systematic modulations of tonic (e.g. with pharmacology) and phasic (e.g. with accessory stimuli; Bruel et al., 2022; Tona et al., 2016) neuromodulator activity may be necessary to disentangle the respective and interactive effects of tonic and phasic neuromodulator activity on human perceptual decision-making.

Reviewer #2 comments:

The main weakness of the paper lies in the strength of evidence provided, and how the results tally with each other. To begin with, there are a lot of significance tests performed here, increasing the chances of false positives. Multiple comparison testing is only performed across time in the EEG results, and not across post-hoc comparisons throughout the paper. In and of itself, it does not invalidate any result per se, but it does colour the interpretation of any results of weak significance, of which there are quite a few. For example, the effect of Drug on d' and subsequent post-hoc comparisons, also effect of ATX on CPP amplitude and others.

We agree with the reviewer that the statistical evidence for some of the results presented in this study is limited. This issue mostly concerns the effects of the pharmacological manipulation (effects of attention were strong and robust), which is unfortunately often the case given the high inter-individual variability in responses to pharmaceutical agents. We have added a paragraph to the Discussion in which we discuss this limitation of the current study. Furthermore, we discuss our findings in the context of previous work, thereby showing that - although not always robust- most of the reported drug effects were in the direction that could be expected based on previous literature. We have pasted that paragraph below.

In Discussion, pages 16:

Although the effects of the attentional manipulation were generally strong and robust, the statistical reliability of the effects of the pharmacological manipulation was more modest for some comparisons. This may partly be explained by high inter-individual variability in responses to pharmaceutical agents. For example, initial levels of catecholamines may modulate the effect of catecholaminergic stimulants on task performance, as task performance is supposed to be optimal at intermediate levels of catecholaminergic neuromodulation (Cools & D’Esposito, 2011). While acknowledging this, we would like to highlight that many of the observed effects of ATX were in the expected direction and in line with previous work. First, pharmacologically enhancing catecholaminergic levels have previously been shown to increase perceptual sensitivity (d’) (Gelbard-Sagiv et al., 2018), a finding that we have replicated here. Second, methylphenidate (MPH), a pharmaceutical agent that elevates catecholaminergic levels as well, has been shown to increase drift rate as derived from drift diffusion modeling on visual tasks (Beste et al., 2018) in line with our ATX observations. Third, a previous study using ATX to elevate catecholaminergic levels observed that ATX increased CPP slope (Loughnane et al., 2019). Although in our case ATX increased the CPP peak and not its slope, this provide causal evidence that centro-parietal ERP signals related to sensory evidence accumulation are modulated by the catecholaminergic system (Nieuwenhuis et al., 2005). Fourth, we observed that elevated levels of catecholamines affected stimulus driven occipital activity relatively late in time and close to the behavioral response, which resonates with previous observations (Gelbard-Sagiv et al., 2018). Finally, ATX had robust effects on physiological responses (heart rate, blood pressure, pupil size), cue-locked ERP signals and oscillatory power dynamics in the alpha-band, leading up to stimulus presentation. We concur, however, that more work is needed to firmly establish how (various forms of) attention and catecholaminergic neuromodulation affect perceptual decision-making.

The lack of an overall RT effect of Drug leaves any DDM result a little underwhelming. How do these results tally? One potential avenue for lack of RT effect in ATX condition is increased drift rate but also increased non-decision time, working against each other. However, it may be difficult to validate these results theoretically.

As the reviewer remarks, an increase in performance/d’ in absence of any RT effects can be algorithmically explained by a combination of increased drift rate and prolonged non-decision time. This is indeed what we observed for ATX. Non-decision time is generally thought to reflect the time necessary for stimulus encoding and motor execution and as such is seen as separate from the evidence-accumulation decision process. We deem it possible that ATX simultaneously prolonged stimulus encoding/motor execution (reflected in changes in non-decision time) and fastened evidence accumulation (reflected in changes in drift rate). Although our neural data did not provide evidence for this claim, previous work has demonstrated that increased baseline (pupil-linked) arousal/neuromodulation is associated with a decreased build-up rate of a neural signal associated with motor execution (β-power over motor cortex, Van Kempen et al., 2019, eLife), potentially linking increased non-decision time under ATX to slowing down of motor execution processes. The same authors also report relationships between baseline (pupil-linked) arousal/neuromodulation and activity over occipital and centroparietal cortices, respectively associated with sensory processing and sensory evidence accumulation, suggesting that baseline neuromodulation may affect all stages leading up to a decision (sensory processing, evidence accumulation and motor execution). Note also that the attentional manipulation seems to simultaneously increase drift rate and shorten non-decision time in our case, as one would expect (Figure 2E, Figure 2 – Supplements 4&5).

There is an interaction between ATX and Cue in terms of drift rate, this goes against the main thesis of the paper of distinct and non-interacting contributions of neuromodulators and attention. This finding is then ignored. There is also a greater EDAN later for ATX compared to PLA later in the results, which would also indicate interaction of neuromodulators and attention but this is also somewhat ignored.

There are indeed some interesting interaction effects between ATX and spatial attention (cue), as pointed out by the reviewer. However, we did also observe striking differences in the effects of ATX and attention on stimulus-locked occipital activity (in timing and spatial specificity) as well as independent (main) effects on CPP amplitude and pre-stimulus alpha power. Therefore, throughout the paper we tried to carefully describe the effects of attention and ATX as largely independently and jointly modulating perceptual decision-making, while at the same time highlighting the interaction effects that we observed, where present. We have highlighted the effects the reviewer refers to even more explicitly in a separate paragraph that we added to the discussion, pasted below.

In Discussion, page 13-14:

We did observe two striking interaction effects between the catecholaminergic system and spatial attention. First, effects of attention on drift rate were increased under catecholaminergic enhancement (Figure 2D). Although this interaction effect was not reflected in CPP slope/peak amplitude, this does suggest that catecholamines and spatial attention might together shape sensory evidence accumulation in a non-linear manner. Second, the amplitude of the cue-locked early lateralized ERP component (resembling the EDAN) was increased under ATX as compared to PLC. The underlying neural processes driving the EDAN ERP, as well as its associated functions, have been a topic of debate. Some have argued that the EDAN reflects early attentional orienting (Praamstra & Kourtis, 2010) but others have claimed it is mere a visually evoked response and reflects visual processing of the cue (Velzen & Eimer, 2003). Thus, whether this effect reflects a modulation of ATX on early attentional processes or rather a modulation of early visual responses to sensory input in general is a matter for future experimentation.

The CPP results are somewhat unclear. Although there is an effect of ATX on drift rate algorithmically, there is no effect of ATX on CPP slope. On the other hand, even though there is no effect of DNP on drift rate, there is an effect of DNP on CPP slope. Perhaps one may say that the effect of DNP on drift rate trended towards significance, but overall the combination of effects here is a little unconvincing. In addition, there is an effect of ATX on CPP amplitude, but how does this tally with behaviour? Would you expect greater CPP amplitude to lead to faster or slower RTs? The authors do recognise this discrepancy in the Discussion, but discount it by saying the relationship between algorithmic and CPP parameters in terms of DDM is unclear, which undermines the reasoning behind the CPP analyses (and especially the one correlating CPP slope with DDM drift rate).

We thank the reviewer for pointing out this dissociation of drug effects in terms of the algorithmic (DDM) and neural (CPP) ‘implementations’ of the evidence accumulating process underlying perceptual decisions. We have added a new paragraph to the discussion where we interpret the effects of ATX on the neural and algorithmic levels of evidence accumulation. Below we have pasted that paragraph:

In Discussion, page 14-15:

We reported attentional and neuromodulatory effects on algorithmic (DDM, Figure 2) and neural (CPP, Figure 3) markers of sensory evidence accumulation. Recent work has started to investigate the association of these two descriptors of the accumulation process, aiming to uncover whether neural activity over centroparietal regions reflects evidence accumulation, as proposed by computational accumulation-to-threshold models (Kelly & O’Connell, 2015; O’Connell et al., 2018; O’Connell & Kelly, 2021; Twomey et al., 2015). Currently, the CPP is often thought to reflect the decision variable, i.e. the (unsigned) evidence for a decision (Twomey et al., 2015), and consequently its slope should correspond with drift rate, whereas its amplitude at any time should correspond with the so-far accumulated evidence. As -computationally- the decision is reached when evidence crosses a decision bound (the threshold), it may be argued that the peak amplitude of the CPP (roughly) corresponds with the decision boundary. This seems to contradict our observation that 1) ATX modulated drift rate, but not CPP slope and 2) ATX did not modulate boundary separation, but did modulate CPP peak. Note, however, that previous studies using pharmacology or pupil-linked indexes of (catecholaminergic) neuromodulation have also demonstrated effects on both CPP peak (van Kempen et al., 2019) and CPP slope (Loughnane et al., 2019).

The posterior component effects are problematic. The main issue is the lack of clarification of and justification for the choice of posterior component. The analysis is introduced in the context of the target selection signal the N2pc/N2c, but the component which follows is defined relative to Cue, albeit post-target. Thus this analysis tells us the effect of Cue on early posterior (possibly) visual ERP components, but it is not related to target selection as it is pooled across target/distractor. Even if we ignore this, the results themselves wrt Drug lack context. There is a trending lower amplitude for ATX at later latencies at temporo-parietal electrodes, and more positive for DNP, relative to PLA. Is this what one would expect given behaviour? This is where the issue of correct component identification becomes critical in order to inform any priors on expected ERP results given behaviour.

We thank the reviewer for raising this issue with the occipital ERP analysis, allowing us to clarify our decisions regarding the analyses and our interpretations of the results. First, the selection of electrodes was based on, and identical to, previous studies investigating lateralized target selection signals in visual tasks containing bilateral visual stimuli (Loughnane et al., 2016; Newman et al., 2017; Papaioannou & Luck, 2020; van Kempen et al., 2019). Second, the ERPs were defined relative to both the direction of the cue as well as the location of the target. As cue direction and target location were not always congruent (cue validity=80%), we could adopt a 2x2 (cue direction x stimulus identity) design for our ERP analyses (we are ignoring drug condition for explanation purposes). For example, for validly cued target trials we extracted two ERP traces: 1) from the hemisphere contralateral to both the cue and the target stimulus (representing processing of cued target stimulus) and 2) from the hemisphere ipsilateral to the cue and the target stimulus (representing processing of non-cued noise stimulus). However, for invalidly cued trials, ERP traces were extracted from 3) the hemisphere contralateral to cue direction and ipsilateral to the target stimulus (reflecting processing of cued noise stimuli) as well as 4) from the hemisphere ipsilateral to cue direction but contralateral to the target stimulus (reflecting processing of non-cued target stimuli). By defining our ERPs as such, we were able to gauge effects of cue direction (reflecting general shifts in attention), stimulus identity (reflecting target vs. noise selection processes) and their interaction (reflecting cue validity) on activity over occipito-temporal activity. Third, we did not pool data (across target/noise stimuli) for statistical analyses, but only for visualization purposes. To clarify how we extracted ERP traces, we have changed Figure 4 substantially. The updated figure now contains a schematic of how these four distinct ERP traces (cue x stimulus identity) were extracted from neural activity. Moreover, for clarity sake, we now show all 12 ERP traces (3x2x2, drug condition x cue direction x stimulus identity) as well as the three main effects that we observed after performing a 3x2x2 repeated measures (rm)ANOVA over time.

We observed robust (cluster-corrected) effects of cue direction (not validity) on early occipital activity (Fig. 4C – left panel) and of stimulus identity (target/noise) and drug condition on later occipital activity (Fig. 4C – middle and right panel). These results crucially highlight the different temporal (early/late) and spatial (lateralized/not lateralized) profiles of cue, target and drug effects on occipital activity. Moreover, we observed a specific order of drug effects on late occipital activity (DNP>PLC>ATX). The behavioral relevance of this pattern of effects remains elusive. Although the effects of drug condition coincide in time with those of target selection (i.e. when activity contralateral and ipsilateral to the target stimulus was different), the effects of drug were bilateral, meaning that occipito-temporal activity related to the processing of the target (task-relevant) stimulus and non-target (task-irrelevant) stimulus was equally modulated by these pharmaceutical agents. One might argue that these effects show that neither ATX nor DNP modulated the signal-to-noise ratio (SNR), a feature that describes how well relevant stimulus information (signal) can be discerned from irrelevant information (noise). Although it may be tempting to extrapolate this finding to behavior, by suggesting that on the basis of these drug effect neither ATX nor DNP could have modulated d’ (behavioral measure describing how well signal is separated from noise), we would like to point out that our behavioral task specifically concerned a discrimination task about the (orientation of the) target stimulus in which the difference between signal and noise was only relevant for localization purposes and thus has a less direct relation with task performance. As such it is difficult to grasp how the modulation of late occipito-temporal activity by ATX and DNP relates to their behavioral effects. Moreover, the bilateral effect of both ATX and DNP also suggests an absence of interaction effects between drug conditions and visuo-spatial attention, as the effects of ATX/DNP were similar across all cue and target identity conditions.

Author Response

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

Cook, Watt, and colleagues previously reported that a mouse model of Spinocerebellar ataxia type 6 (SCA6) displayed defects in BDNF and TrkB levels at an early disease stage. Moreover, they have shown that one month of exercise elevated cerebellar BDNF expression and improved ataxia and cerebellar Purkinje cell firing rate deficits. In the current work, they attempt to define the mechanism underlying the pathophysiological changes occurring in SCA6. For this, they carried out RNA sequencing of cerebellar vermis tissue in 12-month-old SCA6 mice, a time when the disease is already at an advanced stage, and identified widespread dysregulation of many genes involved in the endo-lysosomal system. Focusing on BDNF/TrkB expression, localization, and signaling they found that, in 7-8 month-old SCA6 mice early endosomes are enlarged and accumulate BDNF and TrkB in Purkinje cells. Curiously, TrkB appears to be reduced in the recycling endosomes compartment, despite the fact that recycling endosomes are morphologically normal in SCA6. In addition, the authors describe a reduction in the Late endosomes in SCA6 Purkinje cells associated with reduced BDNF levels and a probable deficit in late endosome maturation.

We would like to thank the reviewers for their careful reading of the paper, their feedback has helped us to add information and experiments to the paper that enhance the clarity of the findings.

Strengths:

The article is well written, and the findings are relevant for the neuropathology of different neurodegenerative diseases where dysfunction of early endosomes is observed. The authors have provided a detailed analysis of the endo-lysosomal system in SCA6 mice. They have shown that TrkB recycling to the cell membrane in recycling endosomes is reduced, and the late endosome transport of BDNF for degradation is impaired. The findings will be crucial in understanding underlying pathology. Lastly, the deficits in early endosomes are rescued by chronic administration of 7,8-DHF.

We thank the reviewers for their positive feedback on this work.

Weaknesses:

The specificity of BDNF and TrkB immunostaining requires additional controls, as it has been very difficult to detect immunostaining of BDNF. In addition, in many of the figures, the background or outside of Purkinje cell boundaries also exhibits a positive signal.

We agree with the reviewers that the performance of the BDNF and TrkB antibodies is an important concern. We have ourselves had difficulties with the performance of many antibodies and the images in this paper are the result of many years of optimization. We have therefore added further detail about the antibody optimization to the methods section of this paper, and have carried out new staining experiments with additional controls. We have added 2 new figure panels in supplementary figures 3 and 4 to demonstrate these tests.

In the case of anti-BDNF antibodies, we have tested several antibodies and staining protocols and found that in our hands, the only antibody that reliably stained BDNF with a good signal to noise ratio was the one used in this paper (abcam ab108319). Even for this antibody, the staining was greatly enhanced by the use of a heat induced epitope retrieval (HIER) step, which allowed the visualization of BDNF within intracellular structures such as endosomes. When we quantified the intensity of this staining in our previous paper, the results were in agreement with those from a BDNF ELISA used to measure levels of BDNF in the cerebellar vermis of WT and SCA6 mice (Cook et al., 2022), which corroborates these results. As the staining was carried out in tissue sections and not dissociated cells, we also see positive signal from the BDNF staining outside of the Purkinje cells, since BDNF acts on cell-surface receptors and is thus released into the extracellular space around cells (Kuczewski et al., 2008) and is detectable in the extracellular matrix (Lam et al., 2019) and presynaptic terminals around neurons (Camuso et al., 2022; Choo et al., 2017). This is in contrast to studies that image BDNF mRNA with in-situ hybridization, which labels BDNF mRNA predominantly found in cells, and cannot tell us about sub-cellular or extracellular localization of BDNF protein. Together, these factors explain why we observe staining that is not cell- limited, but extends into the space around the cells of interest.

We have added an additional supplemental figure to demonstrate the importance of using HIER when staining slices with anti-BDNF (Supplementary figure 3). We tested HIER protocols that involved heating the slices to 95°C in a variety of buffers. The buffers tested were sodium citrate buffer (10 mM sodium citrate, 0.05% Tween 20, pH 6), Tris buffer (10mM TBS, 0.05% Tween 20, pH 10), EDTA buffer (1mM EDTA, 0.05% Tween 20, pH 8) and neutral PBS. The PBS produced the best result, enhancing the staining of both anti-BDNF and anti-EEA1 antibodies (Supplementary figure 3). Therefore all slices stained using those antibodies were heated to 95°C in PBS using a heat block or thermocycler for 10 minutes, then allowed to cool before staining proceeded.

The antibody we use (abcam ab108319) has been used in hundreds of other publications, including Javed et al., 2021 who ectopically expressed BDNF and noted colocalization between the antibody staining and the GFP tag of the BDNF construct, and Lejkowska et al., 2019 who overexpressed BDNF and saw a dramatic increase in antibody staining as well. The colocalization between ectopically expressed BDNF and the antibody in these studies demonstrates the specificity of the antibody.

However, to further validate antibody specificity we used liver tissue as a negative control. In liver tissue from rodents and humans, the majority of the liver contains negligible levels of BDNF (Koppel et al., 2009; Vivacqua et al., 2014), see also the Human Protein Atlas. The exception is some cholangiocytes: epithelial cells that express BDNF at high levels (Vivacqua et al., 2014). We obtained liver tissue from a WT mouse that was undergoing surgery for an unrelated project and fixed and processed the tissue as we did for brain tissue (outlined in methods section). As we would expect, most of the cells in the liver showed BDNF immunoreactivity that was comparable to background levels (Supplementary figure 3). Interestingly, we were also able to detect sparse highly BDNF-positive cells in the liver, presumed cholangiocytes (Supp. Fig. 3). This pattern of liver BDNF expression is as predicted in the literature, and thus acts as a control for our antibody. We therefore believe that in our hands this antibody is able to stain BDNF with an appropriate degree of specificity.

We also carried out staining experiments using a second anti-TrkB antibody that we had previously used to detect TrkB via Western bloing. We carried out immunohistochemistry as previously described using tissue sections from a WT mouse. The staining with the two different antibodies was carried out at the same time and all other reagents were kept constant. We found that both antibodies labelled TrkB in a similar pattern of localization, including in the early endosomes of the Purkinje cells (Supplementary figure 4). The second antibody however did have a lower signal to noise ratio and so we believe that the original anti-TrkB antibody used in this manuscript (EMD Millipore ab9872) is optimal for staining cerebellar tissue sections in our hands.

One important concern about the conclusions is that the RNAseq experiment was conducted in 12-month- old SCA6 mice suggesting that the defects in the endo-lysosomal system may be caused by other pathophysiological events and, likewise, the impairment in BDNF signaling may also be indirect, as also noted by the authors. Indeed, Purkinje cells in SCA6 mice have an impaired ability to degrade other endocytosed cargo beyond BDNF and TrkB, most likely because of trafficking deficits that result in a disruption in the transport of cargo to the lysosomes and lysosomal dysfunction.

We agree with the reviewers that the defects in the endo-lysosomal system may be caused by other events occurring in the course of disease progression. As mentioned by the reviewers, we have noted this possibility in the text. Detailed investigation into the sequence of events and the root causes of signaling disruption in SCA6 merits future study and we aim to address this in future work. We have expanded this explanation in the text.

Moreover, the beneficial effects of 7,8-DHF treatment on motor coordination may be caused by 7,8-DHF properties other than the putative agonist role on TrkB. Indeed, many reservations have been raised about using 7,8-DHF as an agonist of TrkB activity. Several studies have now debunked (Todd et al. PlosONE 2014, PMID: 24503862; Boltaev et al. Sci Signal 2017, PMID: 28831019) or at the very least questioned (Lowe D, Science 2017: see Discussion: https://www.science.org/content/blog-post/those-compounds-aren-t- what-you-think-they-are Wang et al. Cell 2022 PMID: 34963057). Another interpretation is that 7,8-DHF possesses antioxidant activity and neuroprotection against cytotoxicity in HT-22 and PC12 cells, both of which do not express TrkB (Chen et al. Neurosci Lett 201, PMID: 21651962; Han et al. Neurochem Int. 2014, PMID: 24220540). Thus, while this flavonoid may have a beneficial effect on the pathophysiology of SCA6, it is most unlikely that mechanistically this occurs through a TrkB agonistic effect considering the potent anti-oxidant and anti-inflammatory roles of flavonoids in neurodegenerative diseases (Jones et al. Trends Pharmacol Sci 2012, PMID: 22980637).

We thank the reviewers for raising this important point. We have noted in our previous paper (Cook et al., 2022) that 7,8-DHF may not be acting as a TrkB agonist in SCA6 mice, and are in agreement that other explanations are possible. We have now added information to the text of this paper to highlight this possibility. We did show in our previous paper that 7,8-DHF administration activates Akt signaling in the cerebellum of SCA6 mice, a signaling event that is known to take place downstream of TrkB activation. Additionally, 7,8-DHF treatment led to the increase of TrkB levels in the cerebellum of SCA6 mice (Cook et al., 2022), implicating TrkB in the mechanism of action, even if mechanistically, this is not via direct TrkB activation alone. However, even if the mechanism is currently incompletely explained, we believe that 7,8- DHF remains a valuable treatment strategy for SCA6. We have tried to rewrite the Discussion to highlight what we think is the most important takeaway: that 7,8-DHF can rescue endosomal and other deficits in SCA6, even if we do not currently know the full mechanism of action. We have therefore amended the text to add more detail about other potential explanations for the mechanism of action of 7,8-DHF.

References

Camuso S, La Rosa P, Fiorenza MT, Canterini S. 2022. Pleiotropic effects of BDNF on the cerebellum and hippocampus: Implications for neurodevelopmental disorders. Neurobiol Dis. doi:10.1016/j.nbd.2021.105606

Choo M, Miyazaki T, Yamazaki M, Kawamura M, Nakazawa T, Zhang J, Tanimura A, Uesaka N, Watanabe M, Sakimura K, Kano M. 2017. Retrograde BDNF to TrkB signaling promotes synapse elimination in the developing cerebellum. Nat Commun 8:195. doi:10.1038/s41467-017-00260-w

Cook AA, Jayabal S, Sheng J, Fields E, Leung TCS, Quilez S, McNicholas E, Lau L, Huang S, Watt AJ. 2022. Activation of TrkB-Akt signaling rescues deficits in a mouse model of SCA6. Sci Adv 8:3260. doi:10.1126/sciadv.abh3260

Javed S, Lee YJ, Xu J, Huang WH. 2021. Temporal dissection of Rai1 function reveals brain-derived neurotrophic factor as a potential therapeutic target for Smith-Magenis syndrome. Hum Mol Genet 31:275–288. doi:10.1093/HMG/DDAB245

Koppel I, Aid-Pavlidis T, Jaanson K, Sepp M, Pruunsild P, Palm K, Timmusk T. 2009. Tissue-specific and neural activity-regulated expression of human BDNF gene in BAC transgenic mice. BMC Neurosci 10:68. doi:10.1186/1471-2202-10-68

Kuczewski N, Porcher C, Ferrand N, Fiorentino H, Pellegrino C, Kolarow R, Lessmann V, Medina I, Gaiarsa JL. 2008. Backpropagating action potentials trigger dendritic release of BDNF during spontaneous network activity. J Neurosci 28:7013–7023. doi:10.1523/JNEUROSCI.1673-08.2008

Lam D, Enright HA, Cadena J, Peters SKG, Sales AP, Osburn JJ, Soscia DA, Kulp KS, Wheeler EK, Fischer NO. 2019. Tissue-specific extracellular matrix accelerates the formation of neural networks and communities in a neuron-glia co-culture on a multi-electrode array. Sci Rep 9. doi:10.1038/s41598- 019-40128-1

Lejkowska R, Kawa MP, Pius-Sadowska E, Rogińska D, Łuczkowska K, Machaliński B, Machalińska A. 2019. Preclinical Evaluation of Long-Term Neuroprotective Effects of BDNF-Engineered Mesenchymal Stromal Cells as Intravitreal Therapy for Chronic Retinal Degeneration in Rd6 Mutant Mice. Int J Mol Sci 2019, Vol 20, Page 777 20:777. doi:10.3390/IJMS20030777

Vivacqua G, Renzi A, Carpino G, Franchitto A, Gaudio E. 2014. Expression of brain derivated neurotrophic factor and of its receptors: TrKB and p75NT in normal and bile duct ligated rat liver. Ital J Anat Embryol 119:111–129. doi:10.13128/IJAE-15138

Author Response

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

We thank the reviewers and editor for their thoughful and careful evaluation of our manuscript. We appreciate your time and effort and have incorporated many of these suggestions to improve our revised manuscript.

Reviewer #1 (Public Review):

Summary: Cullinan et al. explore the hypothesis that the cytoplasmic N- and C-termini of ASIC1a, not resolved in x-ray or cryo-EM structures, form a dynamic complex that breaks apart at low pH, exposing a C-terminal binding site for RIPK1, a regulator of necrotic cell death. They expressed channels tagged at their N- and C-termini with the fluorescent, non-canonical amino acid ANAP in CHO cells using amber stop-codon suppression. Interaction between the termini was assessed by FRET between ANAP and colored transition metal ions bound either to a cysteine reactive chelator attached to the channel (TETAC) or metal-chelating lipids (C18-NTA). A key advantage to using metal ions is that they are very poor FRET acceptors, i.e. they must be very close to the donor for FRET to occur. This is ideal for measuring small distances/changes in distance on the scales expected from the initial hypothesis. In order to apply chelated metal ions, CHO cells were mechanically unroofed, providing access to the inner leaflet of the plasma membrane. At high pH, the N- and C- termini are close enough for FRET to be measured, but apparently too far apart to be explained by a direct binding interaction. At low pH, there was an apparent increase in FRET between the termini. FRET between ANAP on the N-and Ctermini and metal ions bound to the plasma membrane suggests that both termini move away from the plasma membrane at low pH. The authors propose an alternative hypothesis whereby close association with the plasma membrane precludes RIPK1 binding to the C-terminus of ASIC1a.

Strengths: The findings presented here are certainly valuable for the ion channel/signaling field and the technical approach only increases the significance of the work. The choice of techniques is appropriate for this study and the results are clear and high quality. Sufficient evidence is presented against the starting hypothesis.

Weaknesses: I have a few questions about certain controls and assumptions that I would like to see discussed more explicitly in the manuscript.

My biggest concern is with the C-terminal citrine tag. Might this prevent the hypothesized interaction between the N- and C-termini? What about the serine to cysteine mutations? The authors might consider a control experiment in channels lacking the C-terminal FP tag.

While it is certainly possible that the C-terminal citrine tag is preventing the hypothesized interaction between the intracellular termini, there are a few things that mitigate (but not eliminate) this concern. First, previous work looking at the interaction between the intracellular termini used FPs on both the N- and C-termini and concluded that in fact there is an interaction (PMID:31980622). Our channels have only a single FP, and we use a higher resolution FRET approach. Second, we aVach our citrine tag with a 11-residue linker, allowing for enhanced flexibility of the region and hopefully allowing for more space for an interaction that was posited to be between the very proximal part of the C-terminus (near the membrane and away from the tag) and the untagged N-terminus. Third, we previously showed that Stomatin, a much larger protein than the NTD, could bind the distal C-terminus of rASIC3 with a large fluorescent protein connected by the same linker on the C-terminus. In the case of Stomatin, the interaction involved the residues at the distal portion of the C-terminus close to the bulky FP. Interestingly, while we did not publish this, without this flexible linker, Stomatin could not regulate the channel and likely did not bind.

Despite this, we agree that this is possible and have added a statement in our limitations section explicitly saying this.

Figure 2 supplement 1 shows apparent read-through of the N-terminal stop codons. Given that most of the paper uses N-terminal ANAP tags, this figure should be moved out of the supplement. Do Nterminally truncated subunits form functional channels? Do the authors expect N-terminally truncated subunits to co-assemble in trimers with full-length subunits? The authors should include a more explicit discussion regarding the effect of truncated channels on their FRET signal in the case of such co-assembly.

The positions that show readthrough (E6, L18, H515) were not used in the study. We eliminated them largely on the basis of these westerns. We elected to put the bulk of the blots in the supplement simply because of how many there were. We believe this is the best compromise. It allows us to show representative blots for all our positions without making an illegible figure with 7 blots.

The N-terminally truncated subunits would create very short peptides that are not able to create functional channels. A premature stop at say E8 would create a 7-mer. Our longest N-terminal truncation would only create a protein of 32 amino acids. These don’t contain the transmembrane segments and thus cannot make functional channels.

As the epitope used for the western blots in Figure 2 and supplements is part of the C-terminal tag, these blots do not provide an estimate of the fraction of C-terminally truncated channels (those that failed to incorporate ANAP at the stop codon). What effect would C-terminally truncated channels have on the FRET signal if incorporated into trimers with full-length subunits?

Alternatively, C-terminally truncated subunits would be able to form functional channels because they contain the full N-terminus, the transmembrane domains, the extracellular domain and a portion of the C-terminus. We don’t think this is a major contaminant to our experiments. The only two C-terminal ANAP positions we use are 464 and 505. In each of these cases, they are only used for memFRET. The ones that do not contain ANAP are essentially “invisible” to the experiment. Since we are measuring their proximity to the membrane, having some missing should not maVer. However, there is some chance that truncations in some subunits could allosterically affect the position of the CT in other subunits. We have added a discussion of this in the manuscript.

Some general discussion of these results in the context of trimeric channels would be helpful. Is the putative interaction of the termini within or between subunits? Are the distances between subunits large enough to preclude FRET between donors on one subunit and acceptor ions bound on multiple subunits?

Thank you for this comment. We did not directly test whether the distances are within or between subunits. We considered using a concatemer to do this, however, the concatemeric channels do not express particularly well. Then, UAA incorporation hurts the expression as well. It was unlikely we would be able to get sufficient expression for tmFRET.

However, the Maclean group has previously tested this using FRET between concatenated subunits and determined that FRET is stronger within than between subunits. We have updated the manuscript to reflect a more thorough discussion of our results in the context of their trimeric assembly.

The authors conclude that the relatively small amount of FRET between the cytoplasmic termini suggests that the interaction previously modeled in Rosetta is unlikely. Is it possible that the proposed structure is correct, but labile? For example, could it be that the FRET signal is the time average of a state in which the termini directly interact (as in the Rosetta model) and one in which they do not?

The proposed RoseVa model does not include the reentrant loop of the channel, so it is probable that this model would change if it were redone to include this new feature of the channel.

However, we do discuss the limitation of FRET as a method that measures a time average that is weighted towards closest approach in our discussion section. The termini are most certainly dynamic and it is possible that spend some time in close proximity. Given that FRET is biased towards closest approach, we actually think this strengthens our argument that the termini don’t spend a great deal of time in complex. In addition, our MST data suggests that the termini do not bind. We have added some commentary on this to the discussion section for clarity.

Reviewer #2 (Public Review):

Summary:

The authors use previously characterised FRET methods to measure distances between intracellular segments of ASIC and with the membrane. The distances are measured across different conditions and at multiple positions in a very complete study. The picture that emerges is that the N- and C-termini do not associate.

Strengths:

Good controls, good range of measurements, advanced, well-chosen and carefully performed FRET measurements. The paper is a technical triumph. Particularly, given the weak fluorescence of ANAP, the extent of measurements and the combination with TETAC is noteworthy.

The distance measurements are largely coherent and favour the interpretation that the N and C terminus are not close together as previously claimed.

Weaknesses:

One difficulty is that we do not have a positive control for what binding of something to either N- or Cterminus would look like (either in FRET or otherwise).

We acknowledge that this is a challenge for the approach. Having a positive control for binding would be great but we are not sure such a thing exists. You could certainly imagine a complex between two domains where each label (ANAP and TETAC) are pointed away from one other (giving comparatively modest quenching) or one where they are very close (giving comparatively large quenching), both of which could still be bound. This is essentially a less significant version of the problem with using FPs to measure proximity…they are not very good proxies for the position of the termini. These small labels are certainly beVer proxies but still not perfect. Our conclusion here is based more on the totality of the data. We tried many combinations and saw no sign of distances closer than ~ 20A at resting pH. We think the simplest explanation is that they are not close to one another but we tried to lay out the limitations in the discussion.

One limitation that is not mentioned is the unroofing. The concept of interaction with intracellular domains is being examined. But the authors use unroofing to measure the positions, fully disrupting the cytoplasm. Thus it is not excluded that the unroofing disrupts that interaction. This should be mentioned as a possible (if unlikely) limitation.

Thank you for your comment. We discuss unroofing as a potential limitation because it exposes both sides of the plasma membrane to changes in pH. We have updated this section to include acknowledgement of the possibility that unroofing disrupts the interaction via washout of other critical proteins.

Reviewer #3 (Public Review):

Summary: The manuscript by Cullinan et al., uses ANAP-tmFRET to test the hypothesis that the NTD and CTD form a complex at rest and to probe these domains for acid-induced conformational changes. They find convincing evidence that the NTD and CTD do not have a propensity to form a complex. They also report these domains are parallel to the membrane and that the NTD moves towards, and the CTD away, from the membrane upon acidification.

Strengths:

The major strength of the paper is the use of tmFRET, which excels at measuring short distances and is insensitive to orientation effects. The donor-acceptor pairs here are also great choices as they are minimally disruptive to the structure being studied.

Furthermore, they conduct these measurements over several positions with the N and C tails, both between the tails and to the membrane. Finally, to support their main point, MST is conducted to measure the association of recombinant N and C peptides, finding no evidence of association or complex formation.

Weaknesses:

While tmFRET is a strength, using ANAP as a donor requires the cells to be unroofed to eliminate background signal. This causes two problems. First, it removes any possible low affinity interacting proteins such as actinin (PMID 19028690). Second, the pH changes now occur to both 'extracellular' and 'intracellular' lipid planes. Thus, it is unclear if any conformational changes in the N and CTDs arise from desensitization of the receptor or protonation of specific amino acids in the N or CTDs or even protonation of certain phospholipid groups such as in phosphatidylserine. The authors do comment that prolonged extracellular acidification leads to intracellular acidification as well. But the concerns over disruption by unroofing/washing and relevance of the changes remain.

We acknowledge that unroofing is a limitation of our approach and noted it in the discussion. However, we have updated the section to include the possibility that the act of unroofing and washing could also disrupt the potential interaction between the intracellular domains as well as between these domains and other intracellular proteins. This was the best approach we could use to address our questions and it required that we unroof the cells. However, we look forward to future studies or new techniques that do not require the unroofing of the cells.

The distances calculated depend on the R0 between donor and acceptor. In turn, this depends on the donor's emission spectrum and quantum yield. The spectrum and yield of ANAP is very sensitive to local environment. It is a useful fluorophore for patch fluorometry for precisely this reason, and gating-induced conformational changes in the CTD have been reported just from changes in ANAP emission alone (PMID 29425514). Therefore, using a single R0 value for all positions (and both pHs at a single position) is inappropriate. The authors should either include this caveat and give some estimate of how big an impact changes spectrum and yield might have, or actually measure the emission spectra at all positions tested.

This is a reasonable concern and one we considered. Measuring the quantum yield would be quite difficult. However, we have measured spectra at a number of positions and see a relatively minimal shik in the peak. Most positions peak between 481 and 484nm. If you calculate the difference in R0 using theoretical spectra with a blue shik of 20nm, the difference in R0 is only ~1.5A. A shik of 20nm is on the higher side of anything we have seen in the literature (PMID 30038260) and since even with that large a shik, the difference is minimal we do not think measuring spectra for each position would impact the overall conclusions presented. As you noted, though, the quantum yield also changes. Assuming a change in yield from 0.22 to 0.47, the largest we found reported in the literature (PMID:29923827) , the R0 would increase by 2A. This same paper showed that the blue shiked position was the one with the higher extinction coefficient so these changes would be working in opposition to one another making the difference in R0 even smaller. It is important to note, that while tmFRET is a much more powerful measure of distance than standard FRET, these distances, as you point out, are quite challenging to measure precisely. Our conclusions are based less on the absolute distances and more on the observation that no positions show large quenching and that if there is any change upon acidification, it is in the wrong direction.

Overall, the writing and presentation of figures could be much improved with specific points mentioned in the recommendations for authors section.

See below.

The authors argue that the CTD is largely parallel to the plasma membrane, yet appear to base this conclusion on ANAP to membrane FRET of positions S464 and M505. Two positions is insufficient evidence to support such a claim. Some intermediate positions are needed.

We do not see in the paper where we suggest that the CTD is parallel. However, your point that we could try and determine if this was the case is correct. However, we aVempted to create several other CTD TAG mutants but struggled with readthrough and poor expression of these mutants so we opted to just include S464 and M505. Our point from these data is only that the distal CTD (505) must spend significant time near the membrane to explain our FRET data.

Upon acidification, NTD position Q14 moves towards the plasma membrane (Figure 8B). Q14 also gets closer to C515 or doesn't change relative to 505 (Figures 7C and B) upon acidification. Yet position 505 moves away from the membrane (Figure 8D). How can the NTD move closer to the membrane, and to the CTD but yet the CTD move further from the membrane? Some comment or clarification is needed.

This is a reasonable question and one that is hard to definitively answer. Our goal here was to test the hypothesis that the termini are bound at rest. Mapping the precise positions of the termini is difficult for reasons we will enumerate in the question that asks why we didn’t make a model. There are potentially multiple explanations but the easiest one would be that the CTD could move away from the membrane but closer to Q14, for instance, if the distal termini, say, rotated towards the NTD. This would move 505 closer and have no impact on whether or not the NTD and CTD moved away or toward the membrane.

Reviewer #1 (Recommendations For The Authors):

Minor concerns

The authors show the spectrum of ANAP attached to beads and use this spectrum to calculate R0 for their FRET measurements. Peak ANAP fluorescence is dependent on local environment and many reports show ANAP in protein blue-shiked relative to the values reported here. How would this affect the distance measurements reported?

This is an important point. See above for the answer.

Could the lack of interaction between the N- and C-terminal peptides in Figure 7 arise from the cysteine to serine mutations or lack of structure in the synthetic peptides. How were peptide concentrations measured/verified for the experiment?

It is possible that cysteine to serine mutations could prevent the interaction. It is also possible that these peptides are not capable of adopting their native fold without the presence of the plasma membrane or due to being synthetically created. However, the termini are thought to be largely unstructured. We received these peptides in lyophilized form at >95% purity and resuspended to our desired stock concentration (3 mM C-terminus, 1 mM N-terminus). Even if our concentration was off, we see no signs of interaction up to quite a high concentration.

How was photobleaching measured for correcting the data?

We executed several mock experiments at various TAG positions using either pH 8 and pH 6, where we performed the experiments as usual but with a mock solution exchange when we would normally add the metal. We normalized the L-ANAP fluorescence to the first image and averaged together these values for pH 8 and pH 6. We then corrected using Equation 2 in the manuscript..

We have updated the methods to include how we adjusted for bleaching.

The authors may wish to make it more explicit that their Zn2+ controls also preclude the possibility that a changing FRET signal between ANAP and citrine may affect their data.

Thank you for this comment. We agree, it would strengthen the manuscript to include this statement. We have now included this.

It might be useful to the reader if the authors could include (as a supplement) plots of their data (like in Figure 6), in which FRET efficiency has been converted to distance.

We considered this idea as well but felt like showing the actual data in the figures and the distances in a table would be best.

Figure 5D is mentioned in the text before any other figures. This is unconventional. Could this panel be moved to Figure 1 or the mention moved to later?

Changed

western blot is not capitalized.

Changed.

Figure 1, the ANAP structure shown is the methyl ester, which is presumably cleaved before ANAP is conjugated to the tRNA. The authors may wish to replace this with the free acid structure.

This is a fair point. We originally used the methyl ester structure to indicate the version of ANAP we chose to use. However, you are correct that the methyl ester is cleaved before conjugation to the tRNA. We replaced the methyl ester with the free acid structure to clarify this.

Figures 1 and 4 should have scale bars for the images.

Scale bars have been added to figures 1, 4, and 5.

In Figure 3, the letters in the structures (particularly TETAC) are way too small. Please increase the font size.

Changed

In Figure 3 and Figure 3 supplement 1, the axes are labeled "Absorbance (M-1cm-1)." Absorbance is dimensionless. The authors are likely reporting the extinction coefficient.

Thank you for catching this. We adjusted the axes to extinction coefficient.

In Figures 5 B and C, it might be clearer if the headers read "Initial, +Cu2+/TETAC, DTT" rather than "Initial, FRET, Recovery."

Changed

The panel labels for Figure 8 seem to be out of order.

Changed

The L for L-ANAP should be rendered, by convention, in small caps.

This is a good example of learning something new from the review process. This is the first I have ever heard of small caps. We can find no other papers that use small caps for L-ANAP so I am not 100% sure what convention this is referring to and don’t want to change the wrong thing in the paper. We are happy to change if the editorial staff at eLife agree but have lek this for now.

Reviewer #2 (Recommendations For The Authors):

With so many distances measured, why was not even a basic structural model attempted?

We certainly considered it, but a number of things lead us to conclude that it might imply more certainty about the structure of these termini than we hope to give. 1) Given that the FRET is a time average of positions, these distance constraints would not do much constraining. 2) Given that the termini are likely unstructured and flexible this makes the problem in 1 worse. 3) There is no structural information to use as a starting point for a model. 4) The flexibility of the linkers for each FRET pair also introduces uncertainty. This can, in theory, be modeled as they do in EPR but all of this together made us decide not to do this. What we hope readers take home, is the overall picture of the data is not consistent with the original RIPK1 hypothesis.

Maybe it would be good to draw a band on the graphs in Figure 6 for the FRET signal expected for interaction (and thus, disfavoured by these data). This would at least give context.

We agree this could be helpful, but it is not so easy to do. What distance would we choose? We could put a line at ~5Å (the model predicted distance). As we noted above, a number of distances could be compatible with an interaction. However, we think it’s unlikely that if a complex was formed that none of our measurements would show a distance closer than 20Å at rest and that an unbinding event would then lead to a decrease in distance. This, to us, is the take home message.

Minor points:

"Aker unroofing the cells, only fluorescence associated with the "footprint", or dorsal surface, of the cell membrane is lek behind."

The authors use dorsal and ventral in this section to describe parts of an adherent cell. But in the first instance, they remove the dorsal part of the cell, and then in this phrase, the dorsal part is lek behind....I am a bit confused.

Thank you for pointing out this mistake, we have fixed this. It is indeed the ventral surface lek behind.

"bind at rest an" - and?

Changed

"One previous study used a different approach to try and map the topography of the intracellular termini of ASIC1a comparable to our memFRET experiments." I think a citation is due.

Citation added

"great deal of precedent" even if this result is from my own lab, I would prefer that the authors note that it's one study from one lab! I think best just to delete "great deal of".

“Great deal of” deleted

I think the column "Significance" in the tables is unnecessary when the P value is given.

Thank you for this suggestion. We agree and have made the change.

Figure 7a Q14TAG has a clearly bimodal distribution at pH 8. What could be the meaning of this result? The authors do not mention it that I could find. Perhaps there is no meaning. The authors should state what they think is (or is not) going on.

This is a good question and we don’t have a good answer. It appears to be experimental variability. The data from the “low fret” in this experimental condition all came from the same days. So something was different that day. We considered that they might be outliers to exclude but thought showing all of our data was the beVer path. We reperformed the ANOVA here separating out the “outlier” day and nothing of substance changed. Both populations were still different with P value less than 0.001.

Typo: Lumencore

Changed

Maybe just a matter of taste but the panel created with Biorender in Figure 8 is not attractive and depicts the channel differently to in Figure 5D, which is again different from Figure 1A. Surely one advantage of using computer-generated artwork could be to have consistency.

We agree and have used the same cartoon for all of our images with the one exception being the schematics that are just meant to show the positions that are present in each bar graph.

Figure 4A was squashed to fit (text aspect ratio is wrong).

Fixed

Reviewer #3 (Recommendations For The Authors):

Citrine is used to report incorporation. Yet citrine has a strong tendency to dimerize (PMID 27240257). Did the authors use mCitrine or just Citrine? This is quite important in interpreting their data.

Thank you for pointing out this important distinction. We use mCitirine which we have added to the methods.

The manuscript has numerous instances of imprecise language. For example, page 10, last para, first line, "previous studies have looked at..." or page 7, final paragraph "tell a similar story". Related, the figures could be much better. For example, in Figure 1, where the authors depict the anap chemical in red, as opposed to the blue one might expect of a blue emiqng fluorophore. In figure 6, ANAP is also in red with the quenching group in green. This is opposite to how one typically thinks of FRET with the warmer color being the acceptor not the donor. Moreover, the pH 6 condition is also colored the same shade of red as the ANAP. Labels of Cys positions would again be useful here. In Figure 3, the heteroatoms of TETAC and C18-NTA are very small and difficult to see. It would also be good to label these structures, and the spectra below, so the reader can tell at a glance without looking at the caption, what the structures and spectra arise from. Also, how are the absorption spectra normalized? This is not discussed in the methods. The lack of attention to presentation mars an otherwise nice study.

Thank you for these points. We have made modifications to the manuscript to address these comments.

Abstract, second last line "Aker prolonged acidification, ...", 'prolonged' could be interpreted as 'it takes a while for the domain to move' or 'the movement only happens aker a while'. This not what the authors intend to convey. Consider modifying to just 'Aker acidification,'

We updated the main text to indicate that prolonged acidification is intended to describe acidification that occurs over the minutes timescale.

Pdf page 6, bottom para on Anap incorporation not altering channel function: What is meant by 'steady state pH dependence of activation'? This implies the authors applied a pH stimulus, then waited until equilibrium was achieved ie. until desensitization was complete and measured the current at that point. It seems more likely they simply applied different pH stimuli and measured the peak response and that the use of 'steady state' here is a typo.

We removed the phrase steady state.

Same section, controls of electrophysiology allude to 485, 505 and 515 ANAP-containing channels. In fact, the authors have no way of determining what fraction (if any) of the pH evoked currents arise from channels containing Anap in those positions versus from simply having a translation stop but still functioning. This should be mentioned.

This is correct. We cannot be sure the CTD TAG positions are not a mixture of ANAP-containing channels and truncations. See above for why we do not think this a big concern for the FRET experiments. Functionally, though, you are correct that we cannot tell. We now mention this in the paper.

Methods, the abbreviation for SBT should be defined somewhere.

Added.

Methods, unroofing section, middle paragraph, the authors use nM not nm to list wavelengths of light.

Changed.

Figure 3C-D: There's an unexpected blip in the Anap emission spectra at ~500 nm. Are the grating efficiency of the spectrograph and quantum efficiency of the camera accounted for in these spectra?

This is a good question. The data are not corrected for either camera efficiency or grating efficiency. We don’t have easy access to the actual data (although we can see a pdf version of each). There is a liVle blip in the grating efficiency graph that could partly explain the blip in our spectra.

Figure 5C, were recovery experiments routinely done? If so, would be good to show more than n = 1 in the plot to get an idea of reproducibility.

Recovery experiments were done in every experiment but are not shown for simplicity. We have included all FRET and recovery data for position Q14TAG-C469 at pH 6 in figure 5C to show reproducibility of our FRET and recovery data.

Table 1, considering adding a Δ distance column (pH 8 versus 6) so the magnitude of changes are more easily seen.

This is a reasonable suggestion but we decided not to include a Δ distance column. The data are whole numbers and people can easily determine the Δ distance. We felt that including that column would bring too much focus on what we think are preVy small changes. Our hope is that readers take away that the data are not consistent with complex formation between the determine and focus less on absolute distances.

Figure 7A, Q14tag pH 8 condition has a quite a bit of spread and, likely, two populations. These data, as well as G11, are unlikely to be parametric and hence ANOVA is inappropriate. A normality test, and likely Kruskal-Wallis test is called for.

Aker testing for normality, the data for Q14TAG C485 pH8 are non-normally distributed. However, a Kruskal Wallis is a non-parametric test for a one-way ANOVA and not applicable here. We separated the data out into population 1 and 2 and repeated the two-way ANOVA statistical test. When Q14TAG pH 8 is split into 2 populations, the statistics hardly change. When the data is not separated, Q14TAG pH 8 relative to pH 6 has a p-value <0.0001. When the 2 populations are separated, both populations relative to Q14TAG pH 6 still have a p-value of <0.0001.

Reviewer #1 (Public Review):

Summary:<br /> These types of analyses use many underlying assumptions about the data, which are not easy to verify. Hence, one way to test how the algorithm is performing in a task is to study its performance on synthetic data in which the properties of the variable of interest can be apriori fixed. For example, for burst detection, synthetic data can be generated by injected bursts of known durations, and checking if the algorithm is able to pick it up. Burst detection is difficult in the spectral domain since direct spectral estimators have high variance (see Subhash Chandran et al., 2018, J Neurophysiol). Therefore, detected burst lengths are typically much lower than injected burst lengths (see Figure 3). This problem can be solved by doing burst estimation in the time domain itself, for example, using Matching Pursuit (MP). I think the approach presented in this paper would also work since this model is also trained on data in the time domain. Indeed, the synthetic data can be made more "challenging" by injecting multiple oscillatory bursts that are overlapping in time, for which a greedy approach like MP may fail. It would be very interesting to test whether this method can "keep up" as the data is made more challenging. While showing results from brain signals directly (e.g., Figure 7) is nice, it will be even more impactful if it is backed up with results obtained from synthetic data with known properties.

I was wondering about what kind of "synthetic data" could be used for the results shown in Figure 8-12 but could not come up with a good answer. Perhaps data in which different sensory systems are activated (visual versus auditory) or sensory versus movement epochs are compared to see if the activation maps change as expected. We see similarities between states across multiple runs (reproducibility analysis) and across tasks (e.g. Figure 8 vs 9) and even methods (Figure 8 vs 10), which is great. However, we should also expect the emergence of new modes specific to sensory activation (say auditory cortex for an auditory task). This will allow us to independently check the performance of this method.

The authors should explain the reproducibility results (variational free energy and best run analysis) in the Results section itself, to better orient the reader on what to look for.

Page 15: the comparison across subjects is interesting, but it is not clear why sensory-motor areas show a difference and the mean lifetime of the visual network decreases. Can you please explain this better? The promised discussion in section 3.5 can be expanded as well.

• for: social superorganism - vs human multicellular being, social superorganism, Homni, major evolutionary transition, MET, MET in Individuality, Indyweb, Indranet, Indyweb/Indranet, CCE cumulative cultural evolution, symmathesy, Gyuri Lajos, individual/collective gestalt, interwingled sensemaking, Deep Humanity, DH, meta crisis, meaning crisis, polycrisis

• comment

  • True, there is no physical cohesion that binds human beings together into a larger organism, but there is another dimension - informational cohesion.
  • This informational cohesion expresses itself in cumulative cultural evolution. Even this very discussion they are having is an example of that
  • The social superorganism is therefore composed of an informational body and not a physical one and one can think of its major mentations as collective, consensual ideas such as popular memes, movements, governmental or business actions and policies
  • I slept on this and this morning, realized how salient Adam's question was to my own work
    • The comments here build and expand upon what I thought yesterday (my original annotations)
    • The main connections to my own sense-making work are:
      • Within our specific human species, the deep entanglement between self and other (the terminology that our Deep Humanity praxis terms the "individual / collective gestalt")
      • The Deep Humanity / SRG claim that the concurrent meaning / meta / poly crisis may be an evolutionary test foreshadowing the next possible Major Evolutionary Transition in Individuality.<br /> - https://jonudell.info/h/facet/?max=100&expanded=true&user=stopresetgo&exactTagSearch=true&any=MET+in+Individuality
        • As Adam notes, collective consciousness may be more a metaphorical rather than a literal so a social superorganism, (one reference refers to it as Homni
          • https://www.bbc.com/future/article/20140701-the-superorganism-engulfing-earth
        • may be metaphorical only as this higher order individual lacks the physical signaling system to create a biological coherence that, for instance, an animal body possesses.
        • Nevertheless, the informational connections do exist that bind individual humans together and it is not trivial.
        • Indeed, this is exactly what has catapulted our species into modernity where our cumulative cultural evolution (CCE) has defined the concurrent successes and failures of our species. Modernity's meaning / meta / polycrisis and progress traps are a direct result of CCE.
        • Humanity's intentions and its consequences, both intended and unintended are what has come to shape the entire trajectory of the biosphere. So the impacts of human CCE are not trivial at all. Indeed, a paper has been written proposing that human information systems could be the next Major System Transition (MST) that could lead to another future MET that melds biotic and abiotic
          • https://jonudell.info/h/facet/?max=100&expanded=true&user=stopresetgo&exactTagSearch=true&any=MST+-+information
          • or https://hyp.is/go?url=https%3A%2F%2Fwww.frontiersin.org%2Farticles%2F10.3389%2Ffevo.2021.711556&group=world
        • This circles back to Adam's question and what has just emerged for me is this question:
          • Is it possible that we could evolve in some kind of hybrid direction where we are biologically still separate individuals BUT deeply intertwingled informationally through CCE and something like the theoretical Indyweb/Indranet which is an explicit articulation of our theoretical informational connectivity?
          • In other words, could "collective consciousness be explicitly defined in terms of an explicit, externalized information system reflecting intertwingled individual/collective learning?
      • The Indyweb / Indranet informational laminin protein / connective tissue that informationally binds individuals to others in an explicit, externalized means of connecting the individual informational nodes of the social superorganism, giving it "collective consciousness" (whereas prior to Indyweb / Indranet, this informational laminin/connective tissue was not systematically developed so all informational connection, for example of the existing internet, is incomplete and adhoc)
      • The major trajectory paths that global or localized cultural populations take can become an indication of the behavior of collective consciousness.
        • Voting, both formal and informal is an expression of consensus leading to consensual behavior and the consensual behavior could be a reflection of Homni's collective consciousness

• insight

  • While socially annotating this video, a few insights occurred after last night's sleep:
    • Hypothes.is lacks timebound sequence granularity. Indyweb / Indranet has this feature built in and we need it for social annotation. Why? All the information within this particular annotation cannot be machine sorted into a time series. As the social annotator, I actually have to point out which information came first, second, etc. This entire comment, for instance was written AFTER the original very short annotation. Extra tags were updated to reflect the large comment.
    • I gained a new realization of the relationship and intertwingularity of individual / collective learning while writing and reflecting on this social annotation. I think it's because of Adam's question that really revolves around MET of Individuality and the 3 conversant's questioning of the fluid and fuzzy boundary between "self" and "other"
      • Namely, within Indyweb / Indranet there are two learning pillars that make up the entirety of external sensemaking:
        • the first is social annotation of the work of others
        • the second is our own synthesis of what we learned from others (ie. our social annotations)
      • It is the integration of these two pillars that is the sum of our sensemaking parts. Social annotations allow us to sample the edge of the sensemaking work of others. After all, when we ingest one specific information source of others, it is only one of possibly many. Social annotations reflect how our whole interacts with their part. However, we may then integrate that peripheral information of the other more deeply into our own sensemaking work, and that's where we must have our own central synthesizing Indyweb / Indranet space to do that work.
      • It is this interplay between different poles that constitute CCE and symmathesy, mutual learning.
      • adjacency between
        • Indyweb / Indranet name space
        • Indranet
        • automatic vs manual references / citations
      • adjacency statement
        • Oh man, it's so painful to have to insert all these references and citations when Indranet is designed to do all this! A valuable new meme just emerged to express this:
          • Pain between the existing present situation and the imagined future of the same si the fuel that drives innovation.

• quote: Gien

  • Pain between an existing present situation and an imagined, improved future is the fuel that drives innovation.
• date: 2023, Nov 8

Na przykład analizujemy zachowania użytkowników w naszych usługach, aby stale ulepszać naszą ofertę, sugerujemy oferty, które naszym zdaniem mogą Cię zainteresować i promować nasze własne usługi,

reply to u/Low-Appointment-2906 at https://www.reddit.com/r/books/comments/17pitv9/when_does_annotating_books_become_a_distraction/

Through the middle ages, bookmakers would not only leave significant margins for readers to annotate, but they also illuminated books and included drolleries which readers in the know would use in conjunction with the arts of memory (from rhetoric) to memorize portions of texts more easily. I strongly suspect this isn't what booktokkers are doing; their practice is likely more like the sorts of decorative #ProductivityPorn one sees in the Bullet journal and journaling spaces. It's performative content creation.

Those interested in refining their practices of "reading with a pen in hand", continuing the "great conversation" or having "conversations with their texts" might profitably start with Mortimer J. Adler's essay: “How to Mark a Book” (Saturday Review of Literature, July 6, 1941). In his 1975 KCET series How to Read a Book, which was based on their book of the same name, Adler mentioned to Charles Van Doren that he would buy new copies of books so he could re-annotate them without being distracted by his older annotations.

Some have solved the problem of distracting annotations by interleaving their books so they've got lots of blank space to write their notes. It's a rarer practice now, but some publishers still print Bibles with blank pages every other page for this practice. Others put their annotations and notes into commonplace books or on index cards for their card index/zettelkasten.

As some have mentioned, friends and lovers through time have shared books with annotations as a way of sharing their thoughts. George Custer and his wife Elizabeth did this with Tennyson.

If you're interested in annotating digitally online, perhaps check out Hypothes.is where I've seen teachers and students using social annotation to read and make sense of books [example]. I've also seen groups of people use this tool for hosting online book groups/clubs.

If you're in it for fun, you might appreciate:

• https://archaeologyofreading.org/
• https://booktraces-public.lib.virginia.edu/
• My digital annotations on annotation

And those wishing to delve more deeply into the history and power of annotation might look at: Kalir, Remi H., and Antero Garcia. Annotation. The MIT Press Essential Knowledge Series. MIT Press, 2019. https://mitpressonpubpub.mitpress.mit.edu/annotation.

Good luck annotating! 📝

What a crazy story

Author Response

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

Reviewer #1 (Recommendations for The Authors)

MAJOR CONCERNS

1) Not addressed, but perhaps relevant, is that most of the postembryonic fish growth results from stem cells located in the ciliary marginal zone that make new neurons and Muller glia throughout the fish's life. Thus, Muller cell heterogeneity may result from the central to the peripheral gradient of Muller glial cell maturation.

1a. Müller glial cell heterogeneity needs to be confirmed using, for example, in situ hybridization studies with gene-specific probes identified in the scRNAseq that distinguish these 2 populations. An additional approach could be the use of transgenic lines harboring tagged endogenous or transgene that reflects the promoter activity of the Muller glia subtypespecific gene.

We thank the reviewer for the insightful comments and agree on the importance to substantiate the Müller glia heterogeneity in our manuscript. Our study is not the only study that provides evidence for Müller glia heterogeneity. In particular, we would like to refer to a recent publication (Krylov et al., 2023). Using single cell RNA sequencing, Krylov et al. detect Müller glia heterogeneity in the uninjured retina, as well as upon selective, genetic ablation of distinct subtypes of photoreceptors (e.g. long and short wavelength sensitive cones, as well as rods). They observe six distinct clusters of quiescent Müller glia that show differential spatial distribution along the dorsal/ventral retinal axis. For instance, they report a ventral quiescent Müller glia population that shares some marker genes (aldh1a3, rdh10a, smoc1) with our nonreactive Müller glia 2 (cluster 2, supplementary files 1 and 2). Moreover, the authors report that Müller glia located at different positions along the dorsal/ventral axis exhibit distinct patterns of pcna upregulation as well as subsequent re-activation upon photoreceptor ablation. We have added the supportive information from Krylov et al. in the discussion section (lines: 781-789) of our manuscript.

2) Most interesting, but also least substantiated, is the authors' report of 2 different quiescent Muller glial cell populations in the uninjured retina and 2 different reactive Muller cell populations in the injured retina. If these populations exist independently of each other, it would be important to investigate if they differentially impacted retina regeneration.

2a. CRISPR knockdown in F0 of factors thought to be involved in specific Müller glia-derived progenitor trajectories would be important to lend some functional significance to the data.

We fully agree with the reviewer that addition of functional data would enrich the manuscript with valuable information. However, we don´t believe that the suggested CRISPR knockdown of selected genes in F0 animals (also known as crispants) represents a suitable approach. Crispants have been used successfully to investigate genetic contributions in embryonic-tolarval stages (the first few days) of zebrafish development, as injection of multiple gRNAs targeting the same gene is sufficient to achieve a bi-allelic knockout of the gene of up to 90% (Kroll et al., 2021). However, unless both alleles of the target gene(s) is/are mutated already early on with nearly 100%, it is unlikely that the gRNA inactivation would work equally well during subsequent development into adult stages (several months later, and after exponential growth and volume increase of the animal). Even if biallelic inactivation in the crispants does work early on, it remains unclear whether and how crispants survive to adulthood, which will be necessary in order to address gene function in the context of retina regeneration. Moreover, since we observe that the genetic events during adult retina regeneration are highly similar to the events during retina development, we would rather expect the crispants already display developmental phenotypes, which would further hamper the study of potential regenerationspecific phenotypes in adult animals. We are convinced that only ‘clean’ conditional gene inactivation studies will be suitable to address the impact of Müller glia and derived progenitor trajectories on retina regeneration. In this respect, we have recently developed the new conditional Cre-Controlled CRISPR mutagenesis system (Hans et al., Nature Comm 2021). We are currently establishing stable lines to enable controlled and specific gene inactivation, but have only obtained preliminary results so far; the final analysis will take much more time and is, therefore, beyond the scope of this work.

3) The discussion should be modified to relate the data here presented with those described in Hoang et al., 2020.

We followed the suggestions of the reviewer and compared our single cell RNA sequencing dataset to that described in Hoang et al., 2020. As one might expect, the comparison between the two datasets showed similarities but also significant differences due to the different experimental set-ups. We show the results of this comparison in additional main (new Figure 9) and supplementary figures (new Figure 9-figure supplement 1). In order to compare our newly obtained scRNAseq dataset of MG and MG-lineage-derived cells of the regenerating zebrafish retina to the previously published dataset of light-lesioned retina (Hoang et al., 2020), we employed the ingestion method (Scanpy, https://scanpy-tutorials.readthedocs.io/en/latest/ integrating-data-using-ingest.html) and mapped the clusters identified by Hoang and colleagues to our clusters (new Figure 9). While we applied a short-term lineage tracing strategy and only sequenced the enriched population of FAC-sorted MG and MG-derived cells of the regenerating zebrafish retina, Hoang and colleagues sequenced all retinal cells in the light-lesioned retina. Consequently, comparison between the two datasets uncovered similarities, but also significant differences, due to the different experimental set-ups (Figure 9A). Consistently, the cluster annotated as resting MG in Hoang et al. mapped to clusters annotated as non-reactive MG 1 and 2 in our dataset (new Figure 9B). The cluster annotated as activated MG in Hoang et al. mapped to clusters annotated as reactive MG 1 and 2, as well as to the cluster with hybrid identity of MG/progenitors in our dataset. Interestingly, some cells annotated as activated MG in Hoang et al. mapped also to neurogenic progenitor 2 and 3 clusters in our dataset (Figure 9B). The cluster annotated as progenitors in Hoang et al. mapped to the progenitor area in our dataset, which included neurogenic progenitors 2, 3 as well as photoreceptor and horizontal cell precursors (new Figure 9B). Finally, retinal ganglion cells, cones, GABAergic amacrine cells and bipolar cells annotated in Hoang et al. perfectly mapped to retinal ganglion cells, cone, amacrine and bipolar cells in our dataset (new Figure 9B). While we did not detect a mature horizontal cell cluster, Hoang and colleagues annotated a horizontal cell cluster, which cells mapped to reactive MG 2, MG/progenitors 1 and part of progenitors 3 in our dataset (new Figure 9B). Moreover, Hoang and colleagues annotated rod photoreceptors that mapped to progenitors 3, photoreceptor precursors, red and blue cones, horizontal cell precursors and bipolar cells in our dataset (new Figure 9B). Finally, due to the different cell isolation protocol, Hoang and colleagues annotated additional cell clusters that did not map to any cluster in our more selective dataset, and included oligodendrocytes, pericytes, retinal pigmented epithelial cells as well as vascular/endothelial cells (new Figure 9B). Next, we selected representative marker genes per cluster from our scRNAseq dataset and checked their expression in the dataset by Hoang and colleagues (Figure 9-figure supplement 1). The dot plot showing the expression of selected gene candidates per cluster further corroborated the large overlap between clusters annotated in the present study with those annotated in the study by Hoang and colleagues. These novel comparisons to the data of Hoang et al. are now included in the resubmitted version, and are described and discussed in an additional paragraph in the results (lines: 482-517) as well as discussion (lines: 766-807) sections.

MINOR CONCERNS

1) Fig 1C is difficult to interpret. I am also confused by the color coding which is not presented in the figure legend - why 3 shades of red and two of blue? Please define each (for example, what's the difference between red, purple, and light red in the 6dpl panel?). What are the white areas outlined by blue and red circles/cells (looks like a topography plot)? It appears that there is a fairly large amount of pcna:EGFP expression in the uninjured retina - what are these cells?

We have replaced Figure 1C with a better one and rephrased/extended the explanation of the figure in the results (lines: 192-195). Figure 1C depicts contour plots, which represent the relative frequency of data. Each contour line encloses an equal percentage of events (that is, cells), and contour lines that are closely packed indicate a high concentration of events. In flow cytometry, contour plots are used to represent highly frequent events, as this kind of plots are independent on sample size.

Concerning the observed pcna:EGFP expressing cells in the uninjured retina, we interpret them as proliferating cells coming from the ciliary marginal zone and from Müller glia of the central retina, which represent progenitors and Müller glia that have re-entered the cell cycle to generate rod progenitors, respectively. Consistent with that, we observe pcna:EGFPpositive cells in the ciliary marginal zone as well as central retina using immunofluorescence, as shown in Figure 1-figure supplement 1.

2) Results, lines 186-188 are not presented clearly: EGFP+ cells may persist for some time after they leave the cell cycle, so stating EGFP+ cells are proliferating may not be correct. How long does PCNA promoter activity and EGFP expression remain after Muller cells exit the cell cycle? mCherry+/EGFP- cells may be non-reactive Muller glia or reactive Muller glia that have not entered the cell cycle. It seems likely that Muller glia start reprogramming before undergoing cell division.

We agree with the reviewer that EGFP persists for some time after the cells have left the cell cycle, which we actually describe and use to benefit in our study. We do not know for how long exactly the pcna promoter is active within the cell cycle, but EGFP is known to have a half-life of approximately 24 hours (Li et al., 1998). Even though we cannot make a statement about EGFP persistence in Müller glia, we note that previous reports (Lahne et al., 2015; Nagashima et al., 2013; Nelson et al., 2013; Thummel et al., 2008) and our study (Figure 3-figure supplement 2) show PCNA at the protein level in Müller glia cells between 24 and 48 hpl, including our sampled 44 hpl time point (lines: 69-73). We also agree with the reviewer that Müller glia will become reactive to the injury most likely prior (lines: 67-69) to activation of the pcna promoter, meaning that Müller glia are EGFP-negative at this time point due to the immature status of EGFP after translation. However, we are confident that our data also comprises this cell state (early phase of Müller glia activation) because we sampled proliferating (EGFP- and mCherry-double positive cells) as well as non-proliferating Müller glia (mCherry-only positive cells) at all time points (lines: 213-215 and Figure 1C). We interpret that the early phase of Müller glia activation corresponds to Müller glia transitioning from a nonreactive to a reactive state. With respect to our UMAP, we map this cell state in cluster 1 localizing to the top left part of the cluster, abutting cluster 3, the reactive Müller glia 1 (Figure 2B).

3) I am concerned by the observation that microglia were identified by scRNAseq as a contaminating cell population. Since FACS was based on gfap:mCherry expression, why did microglia end up in the mix? Also, what are the ‘...low-quality cells expressing many ribosomal transcripts...’ and why, if they are low-quality cells, did they pass the sequencing quality control as stated on lines 208-209?

The reviewer is right that microglia should actually not end up in the sample when using the gfap:mCherry line. However, microglia always displayed a certain level of autofluorescence in our experimental set-up (possibly because they may have ingested some cell debris), which may have contributed to their presence in the FACS samples. In contrast to the reviewer, we were not concerned about this ‘contamination’, because the microglia could be easily identified and sorted out using bioinformatics. This is supported by the presented supplementary figure in which microglia separate from the core of clusters containing Müller glia and Müller gliaderived cells in the UMAP of the full dataset (Figure 2-figure supplement 1).

We also acknowledge that ‘low quality cells’ is not an appropriate term for cells in the cluster expressing ribosomal mRNAs at high levels, as ribosomal enrichment actually does not give any information concerning their quality. We referred to them as ‘low quality’ because the enrichment in ribosomal transcripts masks their identity considerably. To correct this, we now renamed cells in this cluster descriptively as ‘ribosomal gene-enriched’ cells (Figure 2-figure supplement 1, line: 226).

4) Fig. 2: please list in the text or fig legend the specific genes used to identify each cell cycle state. Why is cluster 3 considered a reactive Muller population when expressing S phase markers and PCNA? These features seem to distinguish cluster 3 from 4 and may suggest cluster 3 is a progenitor population. Further explanation is necessary to understand the assignments.

Information about the specific genes used to identify each cell cycle state is provided in the paragraph “Bioinformatic analysis” (lines: 925-934) in the Materials and Methods section. We considered listing all the markers in either the results or the figure legends as well, but decided against it, as it impairs readability in our opinion. Nevertheless, we have now highlighted also in the results (line: 261) that the list of cell cycle markers is available in the Materials and Methods section.

We understand the reviewer´s point that cluster 3 represents progenitors and not Müller glia, when PCNA expression is considered as a sole marker of progenitors or of Müller glia reprogrammed to a progenitor state (Hoang et al., 2020). However, we disagree with this view for three reasons. First, although PCNA is used as a marker of Müller glia reprogrammed to a progenitor state and of progenitors in Hoang et al., 2020, it should be noted that PCNA-positive, Müller glia cells are present in the central retina already in uninjured conditions, when regeneration-associated, Müller glia-derived progenitors are not detectable. Second, cluster 3 is evident only at 44 hpl, a time point at which Müller glia cells are about to divide or have undergone their first and only cell division. In this regard, we would like to refer to the discussion about Müller glia and Müller glia-derived progenitors as distinct populations in Lenkowski and Raymond, 2014. Third, we have performed in situ hybridization for starmaker (stm), a marker gene highly specific for cells in cluster 3 (supplementary files 1 and 3), combined with immunohistochemistry for GFAP and PCNA. The results of the staining are depicted in a new Figure 3-figure supplement 2. In strong agreement with our sequencing results, we observe stm expression only at 44 hpl, whereas no signal is detected in the uninjured as well as 4 and 6 dpl retina (Figure 3- figure supplement 2). Virtually all stm-positive cells at 44 hpl are also PCNA- and GFAP-double positive cells displaying a clear Müller glia morphology (Figure 3- figure supplement 2). Hence, we interpret cells in cluster 3 as reactive Müller glia, indicating that pcna can be used as a marker of progenitors, but not exclusively of progenitors, prevalently at later stages. At 44 hpl, Müller glia express pcna in order to undergo asymmetric cell division giving rise to the renewed Müller glia and the multipotent progenitor that will continue dividing.

5) I am confused by the crlf1a scRNAseq data indicating it is associated with proliferating PCNA+ reactive Muller glia Cluster 3 and PCNA- reactive Muller glia Cluster4 at 44 hpl (Fig. 3), yet in Fig. 4 crlf1a in situ signal is exclusively associated with proliferating Muller glia at 44 hpl. Why don't we observe the crlf1a+/PCNA- cell population?

We highlight that crlf1a expression is actually detected also at 4 dpl (Fig. 3). We also note that immunofluorescence in Fig 3. shows crlf1a mRNA and PCNA protein, whereas single cell RNA sequencing detects crlf1a and pcna transcripts. In this context, it is possible that crlf1a-, PCNAdouble positive cells detected at 4 dpl are still positive for the PCNA protein, but no longer express the pcna transcript. Double in situ hybridization for pcna and crlf1a would be needed to fully address whether crlf1a-positive cells are still pcna-positive at 4 dpl. It is also possible that crlf1a-, GFAP-double positive, PCNA-negative Müller glia are fewer and only masked in the crowd of crlf1a-, PCNA-double positive, GFAP-negative progenitors at 4 dpl (Raymond et al., 2006). We amended the discussion section with this information (lines: 634-654).

6) scRNAseq cluster 3 is a proliferating population that is assigned "reactive Muller glia", whereas cluster 5 is assigned Muller glia/progenitor and in the Discussion referred to as MG about to go or already underwent asymmetric division to generate a progenitor (lines 568-571). I don't understand why cluster 3 is not referred to as the one harboring reactive MG/progenitors that underwent or are undergoing asymmetric cell division - The timing is right, as are the markers.

We would like to refer the reviewer to the discussion in point 4, including the changes we introduced in the Materials and Methods (Lines 925-934). As mentioned above, we do not agree that PCNA alone represents an exclusive marker of progenitors, but is rather a marker of cells undergoing proliferation. Moreover, we note that Müller glia first and only division occurs between 31 and 48 hpl. Finally, as mentioned above, expression of stm is a unique marker for cluster 3, which is only evident at 44 hpl, but not of cluster 5, which is evident at 4 dpl.

It seems cluster 5 might better fit the amplifying progenitor stage where some MG markers are retained but diluted by cell division. Please clarify the reasoning behind the labeling of this cluster. It is not clear why this cluster has to contain self-renewed Muller glia - why wouldn't these Muller cells partition to quiescent MG clusters 1 and 2 or reactive Muller glia in clusters 3 and 4?

We partially agree with the reviewer that cluster 5 might better fit the amplifying progenitor state, and this is why we indicate this cluster as a “crossroad in the trajectory” in the discussion (lines: 613-631). However, we cannot entirely exclude that cells in cluster 5 contain selfrenewed Müller glia (differential gene expression analysis highlights glial markers too, see Figure 3A, supplementary file 6). Cells that we interpret as self-renewing Müller glia do not partition back to quiescent Müller glia (cluster 1 and 2) because they are on the way to be quiescent Müller glia again, yet they did not reach that point, maybe due to sampling reasons. Unfortunately, our short-term lineage tracing strategy ceases at 6 dpl. We also speculate in the discussion (lines: 679-682) that if we had sampled at later time points (e.g. at 14 dpl), we might have been able to detect the density of the cells in the glial area moving back to clusters 1 or 2 (cell density plots, Figure 2B).

I also have trouble understanding cluster 4's assignment. The Discussion states it represents cells at the crossroad of glial and neurogenic trajectory containing self-renewed Muller glia as well as first-born MG-derived progenitors. However, it is populated by cells after 44 hpl (Fig. 2B) which is when reactive Muller glia are detected and lacks proliferative markers.

We think that there is a misunderstanding here. We never refer to cluster 4 as a crossroad in the glial and neurogenic trajectory. We state that cluster 5 is actually the crossroad between the two trajectories (line 629). We further propose that self-renewed MG close the cycle via late reactive MG (cluster 4) and return into non-reactive Müller glia (clusters 1 and 2, red, dashed line in Figure 10) (now described in lines 631-633). The cell density plots support the direction of the cycle closing towards non-reactive Müller glia, in particular at 4 and 6 dpl (Figure 2B).

Might cluster 4 represent a population of reactive MG remaining at 4 dpl that never entered the cell cycle and therefore would be devoid of Muller glia-derived progenitors?

As stated in the manuscript, we actually think that marker expression as well as the cell density plots support our assignment of cluster 4 to represent self-renewed Müller glia closing the cycle to non-reactive Müller glia. Our assignment also fits well with the expected events following asymmetric cell division. However, as we cannot rule out the reviewer´s entire idea, we included the suggestion in the updated discussion (lines 651-654).

7) Results, lines 163-164; Please provide a reference for "..... consistent with the previously described....."

We thank the reviewer for this observation and we added the appropriate references (Fimbel et al., 2007; Lenkowski and Raymond, 2014; Thummel et al., 2008) in the updated version of the manuscript (lines: 171-172).

Reviewer #2 (Recommendations For The Authors):

Overall, this very thorough study provides interesting and unexpected results. The published data set will be useful for many subsequent studies. I have only a few remarks that the authors may consider discussing. Their cluster analysis revealed most of the expected cell clusters with some interesting surprises. One relates to photoreceptors where the authors describe well-separated clusters for red and green cones, while rods, UV and blue cones do not form clusters. For rods, this is discussed, but I miss a brief discussion on the "missing" cone subtypes.

We thank the reviewer for the insightful comments. It is correct that we indeed detect only red and blue cones, as indicated by their expression of red-sensitive opsin gene (opn1lw2) and the blue-sensitive opsin gene (opn1sw2), respectively. It is possible that missing cone subtypes are born later than 6 dpl. As the reviewer suggested, we amended the discussion and added information about the missing cone subtypes (lines: 724-726).

I am also intrigued by the two, quite separated amacrine cell clusters, while bipolar cells cluster in one cluster, without separation in (say) ON and OFF bipolar cells. This may also merit a discussion. What are their ideas on the small and quite separated amacrine cell cluster (cluster 14).

Bipolar cells in cluster 15 are very sparse in our dataset, with only 40 cells in total. Hence, the sample size might be too small to be separated into ON and OFF subtypes. Alternatively, cells might be still immature, as we use 6 dpl as our latest sampled time point. Concerning cells in cluster 14, we think they are starburst amacrine cells, as indicated by their simultaneous expression of gad1b and chata (Figure 8-figure supplement 2B), which is a characteristic feature of starburst amacrine cells in mouse (O´Malley et al., 1992). We added this observation in the discussion (lines: 706-712).

Author Response

The following is the authors’ response to the previous reviews

Reviewer #1 (Public Review):

Comments on the original submission:

Trypanosoma brucei undergoes antigenic variation to evade the mammalian host's immune response. To achieve this, T. brucei regularly expresses different VSGs as its major surface antigen. VSG expression sites are exclusively subtelomeric, and VSG transcription by RNA polymerase I is strictly monoallelic. It has been shown that T. brucei RAP1, a telomeric protein, and the phosphoinositol pathway are essential for VSG monoallelic expression. In previous studies, Cestari et al. (ref. 24) has shown that PIP5pase interacts with RAP1 and that RAP1 binds PI(3,4,5)P3. RNAseq and ChIPseq analyses have been performed previously in PIP5pase conditional knockout cells, too (ref. 24). In the current study, Touray et al. did similar analyses except that catalytic dead PIP5pase mutant was used and the DNA and PI(3,4,5)P3 binding activities of RAP1 fragments were examined. Specifically, the authors examined the transcriptome profile and did RAP1 ChIPseq in PIP5pase catalytic dead mutant. The authors also expressed several C-terminal His6-tagged RAP1 recombinant proteins (full-length, aa1300, aa301-560, and aa 561-855). These fragments' DNA binding activities were examined by EMSA analysis and their phosphoinositides binding activities were examined by affinity pulldown of biotin-conjugated phosphoinositides. As a result, the authors confirmed that VSG silencing (both BES-linked and MES-linked VSGs) depends on PIP5pase catalytic activity, but the overall knowledge improvement is incremental. The most convincing data come from the phosphoinositide binding assay as it clearly shows that N-terminus of RAP1 binds PI(3,4,5)P3 but not PI(4,5)P2, although this is only assayed in vitro, while the in vivo binding of full-length RAP1 to PI(3,4,5)P3 has been previously published by Cestari et al (ref. 24) already. Considering that many phosphoinositides exert their regulatory role by modulate the subcellular localization of their bound proteins, it is reasonable to hypothesize that binding to PI(3,4,5)P3 can remove RAP1 from the chromatin. However, no convincing data have been shown to support the author's hypothesis that this regulation is through an "allosteric switch".

Comments on revised manuscript:

In this revised manuscript, Touray et al. have responded to reviewers' comments with some revisions satisfactorily. However, the authors still haven't addressed some key scientific rigor issues, which are listed below:

1) It is critical to clearly state whether the observations are made for the endogenous WT protein or the tagged protein. It is good that the authors currently clearly indicate the results observed in vivo are for the RAP1-HA protein. However, this is not as clearly stated for in vitro EMSA analyses. In addition, in discussion, the authors simply assumed that the c-terminally tagged RAP1 behaves the same as WT RAP1 and all conclusions were made about WT RAP1.

There are two choices here. The authors can validate that RAP1-HA still retains RAP1's essential function as a sole allele in T. brucei cells (as was recommended previously). Indeed, HA-tagged RAP1 has been studied before, but it is the N-terminally HA-tagged RAP1 that has been shown to retain its essential functions. Adding the HA tag to the C-terminus of RAP1 may well cause certain defects to RAP1. For example, N-terminally HA-tagged TERT does not complement the telomere shortening phenotype in TERT null T. brucei cells, while C-terminally GFP-tagged TERT does, indicating that HA-TERT is not fully functional while TERT-GFP likely has its essential functions (Dreesen, RU thesis). Although RAP1-HA behaves similar to WT RAP1 in many ways, it is still not fully validated that this protein retains essential functions of RAP1. By the way, it has been published that cells lacking one allele of RAP1 behave as WT cells for cell growth and VSG silencing (Yang et al. 2009, Cell; Afrin et al. 2020, mSphere). In addition, although RAP1 may interact with TRF weakly, the interaction is direct, as shown in yeast 2-hybrid analysis in (Yang et al. 2009, Cell).

Alternatively, if the authors do not wish to validate the functionality of RAP1-HA, they need to add one paragraph at the beginning of the discussion to clearly state that RAP1-HA may not behave exactly as WT RAP1. This is important for readers to better interpret the results. In addition, the authors need to tune down the current conclusions dramatically, as all described observations are made on RAP1-HA but not the WT RAP1.

The results with RAP1-HA are consistent with previous knowledge of RAP1 interactions with telomeric proteins and DNA. Hence, the C-terminal HA-tagged RAP1 seems, by all measures, functional. Nevertheless, to make it clear for the reader, we added a note in the discussion, lines 244-246: “Although we showed that C-terminal HA-tagged RAP1 protein has telomeric localization (Cestari et al. 2015, PNAS) and interactions with other telomeric proteins (Cestari et al. 2019 Mol Cell Biol); we cannot rule out potential differences between HA-tagged and non tagged RAP1.”

For a similar reason, the current EMSA results truly reflect how C-terminally His6-tagged RAP1 and RAP1 fragments behave. If the authors choose not to remove the His6 tag, it is essential that they use "RAP1-His6" to refer to these recombinant proteins. It is also essential for the authors to clearly state in the discussion that the tagged RAP1 fragments bind DNA, but the current data do not reveal whether WT RAP1 binds DNA. In addition, the authors incorrectly stated that "disruption of the MybL domain sequence did not eliminate RAP1-telomere binding in vivo" (lines 165-166). In ref 29, deletion of Myb domain did not abolish RAP1-telomere association. However, point mutations in MybL domain that abolish RAP1's DNA binding activities clearly disrupted RAP1's association with the telomere chromatin. Therefore, the current observation is not completely consistent with that published in ref 29.

We stated in line 149-150 “…we expressed and purified from E. coli recombinant 6xHistagged T. brucei RAP1 (rRAP1)”. To clarify to the authors, we replaced rRAP1 with rRAP1-His throughout the manuscript and figures. As for the statement that “disruption of the MybL domain sequence did not eliminate RAP1-telomere binding in vivo" (lines 165-166).”. We removed the statement from the manuscript.

2) There is no evidence, in vitro or in vivo, that binding PI(3,4,5)P3 to RAP1 causes conformational change in RAP1. The BRCT domain of RAP1 is known for its ability to homodimerize (Afrin et al. 2020, mSphere). It is therefore possible that binding of PI(3,4,5)P3 to RAP1 simply disrupts its homodimerization function. The authors clearly have extrapolated their conclusions based on available data. It is therefore important to revise the discussion and make appropriate statements.

We did not state that PI(3,4,5)P3 causes RAP1 conformational changes. We discussed the possibility. We stated in lines 199-201: “PI(3,4,5)P3 inhibition of RAP1-DNA binding might be due to its association with RAP1 N-terminus causing conformational changes that affect Myb and MybL domains association with DNA.” This is a reasonable discussion, given the data presented in the manuscript.

Reviewer #2 (Public Review):

In this manuscript, Touray et al investigate the mechanisms by which PIP5Pase and RAP1 control VSG expression in T. brucei and demonstrate an important role for this enzyme in a signalling pathway that likely plays a role in antigenic variation in T. brucei. While these data do not definitively show a role for this pathway in antigenic variation, the data are critical for establishing this pathway as a potential way the parasite could control antigenic variation and thus represent a fundamental discovery.

The methods used in the study are generally well-controlled. The authors provide evidence that RAP1 binds to PI(3,4,5)P3 through its N-terminus and that this binding regulates RAP1 binding to VSG expression sites, which in turn regulates VSG silencing. Overall their results support the conclusions made in the manuscript. Readers should take into consideration that the epitope tags on RAP1 could alter its function, however.

There are a few small caveats that are worth noting. First, the analysis of VSG derepression and switching in Figure 1 relies on a genome which does not contain minichromosomal (MC) VSG sequences. This means that MC VSGs could theoretically be mis-assigned as coming from another genomic location in the absence of an MC reference. As the origin of the VSGs in these clones isn't a major point in the paper, I do not think this is a major concern, but I would not over-interpret the particular details of switching outcomes in these experiments.

We agree with the reviewer and thus made no speculations on minichromosomes. The data analysis must rely on the available genome, and the reference genome used is well-assembled with PacBio sequences and Hi-C data (Muller et al. 2018, Nature).

Another aspect of this work that is perhaps important, but not discussed much by the authors, is the fact that signalling is extremely poorly understood in T. brucei. In Figure 1B, the RNA-seq data show many genes upregulated after expression of the Mut PIP5Pase (not just VSGs). The authors rightly avoid claiming that this pathway is exclusive to VSGs, but I wonder if these data could provide insight into the other biological processes that might be controlled by this signaling pathway in T. brucei.

We published that the inositol phosphate pathway also plays a role in T. brucei development (Cestari et al. 2018, Mol Biol Cell; reviewed by Cestari I 2020, PLOS Pathogens)

Overall, this is an excellent study which represents an important step forward in understanding how antigenic variation is controlled in T. brucei. The possibility that this process could be controlled via a signalling pathway has been speculated for a long time, and this study provides the first mechanistic evidence for that possibility.

Reviewer #1 (Recommendations For The Authors):

Please see the public review for recommendations.1. It is critical to clearly state whether the observations are made for the endogenous WT protein or the tagged protein. It is good that the authors currently clearly indicate the results observed in vivo are for the RAP1-HA protein. However, this is not as clearly stated for in vitro EMSA analyses. In addition, in discussion, the authors simply assumed that the c-terminally tagged RAP1 behaves the same as WT RAP1 and all conclusions were made about WT RAP1.

There are two choices here. The authors can validate that RAP1-HA still retains RAP1's essential function as a sole allele in T. brucei cells (as was recommended previously). Indeed, HA-tagged RAP1 has been studied before, but it is the N-terminally HA-tagged RAP1 that has been shown to retain its essential functions. Adding the HA tag to the C-terminus of RAP1 may well cause certain defects to RAP1. For example, N-terminally HA-tagged TERT does not complement the telomere shortening phenotype in TERT null T. brucei cells, while C-terminally GFP-tagged TERT does, indicating that HA-TERT is not fully functional while TERT-GFP likely has its essential functions (Dreesen, RU thesis). Although RAP1-HA behaves similar to WT RAP1 in many ways, it is still not fully validated that this protein retains essential functions of RAP1. By the way, it has been published that cells lacking one allele of RAP1 behaves as WT cells for cell growth and VSG silencing (Yang et al. 2009, Cell; Afrin et al. 2020, mSphere). In addition, although RAP1 may interact with TRF weakly, the interaction is direct, as shown in yeast 2-hybrid analysis in (Yang et al. 2009, Cell).

Alternatively, if the authors do not wish to validate the functionality of RAP1-HA, they need to add one paragraph at the beginning of the discussion to clearly state that RAP1-HA may not behave exactly as WT RAP1. This is important for readers to better interpret the results. In addition, the authors need to tune down the current conclusions dramatically, as all described observations are made on RAP1-HA but not the WT RAP1.

The results with RAP1-HA are consistent with previous knowledge of RAP1 interactions with telomeric proteins and DNA. Hence, the C-terminal HA-tagged RAP1 seems, by all measures, functional. Nevertheless, to make it clear for the reader, we added a note in the discussion, lines 244-246: “Although we showed that C-terminal HA-tagged RAP1 protein has telomeric localization (Cestari et al. 2015, PNAS) and interactions with other telomeric proteins (Cestari et al. 2019 Mol Cell Biol); we cannot rule out potential differences between HA-tagged and non tagged RAP1.”

For a similar reason, the current EMSA results truly reflect how C-terminally His6-tagged RAP1 and RAP1 fragments behave. If the authors choose not to remove the His6 tag, it is essential that they use "RAP1-His6" to refer to these recombinant proteins. It is also essential for the authors to clearly state in the discussion that the tagged RAP1 fragments bind DNA, but the current data do not reveal whether WT RAP1 binds DNA. In addition, the authors incorrectly stated that "disruption of the MybL domain sequence did not eliminate RAP1-telomere binding in vivo" (lines 165-166). In ref 29, deletion of Myb domain did not abolish RAP1-telomere association. However, point mutations in MybL domain that abolish RAP1's DNA binding activities clearly disrupted RAP1's association with the telomere chromatin. Therefore, the current observation is not completely consistent with that published in ref 29.

We stated in lines 149-150 “…we expressed and purified from E. coli recombinant 6xHistagged T. brucei RAP1 (rRAP1)”. To clarify to the authors, we replaced rRAP1 with rRAP1-His throughout the manuscript text. As for the statement that “disruption of the MybL domain sequence did not eliminate RAP1telomere binding in vivo" (lines 165-166).”. We removed the statement from the manuscript.

2) There is no evidence, in vitro or in vivo, that binding PI(3,4,5)P3 to RAP1 causes conformational change in RAP1. The BRCT domain of RAP1 is known for its ability to homodimerize (Afrin et al. 2020, mSphere). It is therefore possible that binding of PI(3,4,5)P3 to RAP1 simply disrupts its homodimerization function. The authors clearly have extrapolated their conclusions based on available data. It is therefore important to revise the discussion and make appropriate statements.

We did not state that PI(3,4,5)P3 causes RAP1 conformational changes. We discussed the possibility. We stated in lines 199-201: “PI(3,4,5)P3 inhibition of RAP1-DNA binding might be due to its association with RAP1 N-terminus causing conformational changes that affect Myb and MybL domains association with DNA.” This is a reasonable discussion, given the data presented in the manuscript.

Author Response

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

We greatly appreciate the valuable and constructive review of our manuscript. The reviewers’ comments have helped us to improve the quality of the paper. Here we provide detailed responses to the reviewers’ comments and discuss the new experiments we performed.

Reviewer #1

Summary:

In this study, the authors generate a Drosophila model to assess disease-linked allelic variants in the UBA5 gene. In humans, variants in UBA5 have been associated with DEE44, characterized by developmental delay, seizures, and encephalopathy. Here, the authors set out to characterize the relationship between 12 disease-linked variants in UBA5 using a variety of assays in their Drosophila Uba5 model. They first show that human UBA5 can substitute all essential functions of the Drosophila Uba5 ortholog, and then assess phenotypes in flies expressing the various disease variants. Using these assays, the authors classify the alleles into mild, intermediate, and severe loss-of-function alleles. Further, the authors establish several important in vitro assays to determine the impacts of the disease alleles on Uba5 stability and function. Together, they find a relatively close correlation between in vivo and in vitro relationships between Uba5 alleles and establish a new Drosophila model to probe the etiology of Uba5-related disorders.

Strengths:

Overall, this is a convincing and well-executed study. There is clearly a need to assess disease-associated allelic variants to better understand human disorders, particularly for rare diseases, and this humanized fly model of Uba5 is a powerful system to rapidly evaluate variants and relationships to various phenotypes. The manuscript is well written, and the experiments are appropriately controlled.

Recommendations For The Authors:

1) It would seem of value to determine what tissue(s) the essential function of Uba5 resides. The authors nicely detail the expression of Uba5 in a subset of neurons and glia, and indicate it is expressed in a variety of other tissues. Null mutants are embryonic lethal, suggesting an essential function. From the mouse study cited, it appears Uba5 functions early in development in the hematopoietic system. The authors can express their UAS-Uba5 rescue construct using a variety of tissue-specific Gal4 lines to determine whether the essential function of Uba5 is in the nervous system or other tissues, which would be of interest in understanding key functions of Uba5.

We thank the reviewer for the suggestion. We tried to rescue the lethality of the Uba5 mutants by expressing human UBA5 reference protein in different tissues. We found that ubiquitous expression of UBA5 (da-GAL4 or act-GAL4) successfully rescues the lethality, however, expression of UBA5 in neurons (elav-GAL4), glia (repo-GAL4), or both neurons and glia does not. In addition, expression of UBA5 in fat body (SPARC-GAL4) or muscles (Mef2-GAL4) does not rescue the lethality either. These results suggest that Uba5 is required in multiple tissues in flies. These data are included in the revised manuscript.

2). Do intermediate Uba5 alleles impact synaptic function or growth? The etiology of the disease is linked with epilepsy and neurodevelopmental disorders, and the interesting parallels the authors note between Uba5 and Para expression indicate perhaps shared roles in neurons that drive firing activity. Together, these lines of evidence may suggest the Uba5 alleles may have possible impacts on synaptic growth, morphology, and/or function. It would be of interest to examine the larval neuromuscular junction and assess NMJ growth, morphology, and perform some basic electrophysiology to determine if there are any functional defects.

Following the reviewer’s suggestion, we tested the morphology of NMJs in the humanized flies. We did not observe any obvious changes in the number or size of the synaptic boutons caused by the Group II variants. Hence, we conclude that the Uba5 variants do not cause an obvious defect in synaptic growth. The results are included in the Figure S3.

More generally, can the authors comment on the expression pattern of Uba5? One might consider something like Uba5 to be a "housekeeping" gene and expressed/required in most if not all cell types. From the data presented in Fig. 2, it appears expression is more sparse, perhaps, as the authors point out, because of roles in mature neurons that actively fire (like Para). Are neuronal targets of Uba5 known, which might suggest key pathways it modulates?

We showed that Uba5 is broadly expressed in third instar larvae. FlyAtlas2 and FlyCellAtlas datasets show that Uba5 is broadly expressed but not in all the cells. In the larval CNS and adult brain, Uba5 is not expressed in all cells either. Hence, we cannot say Uba5 is a “housekeeping” gene. Regarding the neuronal targets of Uba5, we do not know which types of neurons express Uba5 and which pathways Uba5 modulates. This could be studied in the future.

3) Does strong overexpression of the various Uba5 alleles in otherwise wild-type flies cause any phenotypes? This might support possible antimorphic/dominant negative functions of some of the variants. Is it plausible that any of the alleles could impact oligomerization of Uba5?

We have not observed compromised viability or any obvious phenotype in flies overexpressing human reference UBA5 or UBA5 variants. So, our results do not support a dominant negative effect of any of the variants.

To our knowledge, people do not have sufficient knowledge on UBA5 dimerization to speculate on whether some variants could play a dominant negative role. There is one variant, V260M, that lies at the dimer interface. We showed that the V260M variant biochemically affects ATP binding as well as UFM1 activation, but we do not have evidence to support that it causes dominant negative effects by affecting UBA5 dimerization.

Minor points:

1) Page 5 line 45: It seems a reference is missing about the temperature dependence of Gal4 activity.

We apologize for the missing reference. We have incorporated a reference to PMID 25824290.

2) It might be of interest to assay the various transgenic rescue alleles at a higher temperature (say 29C) in addition to the nice work looking at 18/25C survival. Perhaps some of the alleles display temperature sensitivity at low (18) and high (29) temperatures.

We now include the survival rate data at 29C. The enzyme dead and severe LoF variants fail to rescue the lethality at 29C, while the mild (Group IA and IB) variants fully rescue. For the three Group II variants, the survival rate at 29C is higher than that at 25C and 18C. The results support the dosage sensitive effects of UBA5 overexpression, but do not support any variant to be temperature sensitive within this range.

Reviewer #2

Relative simplicity and genetic accessibility of the fly brain make it a premier model system for studying the function of genes linked to various diseases in humans. Here, Pan et al. show that human UBA5, whose mutations cause developmental and epileptic encephalopathy, can functionally replace the fly homolog Uba5. The authors then systematically express in flies the different versions of the gene carrying clinically relevant SNPs and perform extensive phenotypic characterization such as survival rate, developmental timing, lifespan, locomotor and seizure activity, as well as in vitro biochemical characterization (stability, ATP binding, UFM-1 activation) of the corresponding recombinant proteins. The biochemical effects are well predicted by (or at least consistent with) the location of affected amino acids in the previously described Uba5 protein structure. Most strikingly, the severity of biochemical defects appears to closely track the severity of phenotypic defects observed in vivo in flies. While the paper does not provide many novel insights into the function of Uba5, it convincingly establishes the fly nervous system as a powerful model for future mechanistic studies.

One potential limitation is the design of the expression system in this work. Even though the authors state that "human cDNA is expressed under the control of the endogenous Uba5 enhancer and promoter", it is in fact the Gal4 gene that is expressed from the endogenous locus, meaning that the cDNA expression level would inevitably be amplified in comparison. The fact that different effects were observed when some experiments were performed at different temperatures (18 vs. 25) is also consistent with this. While I do not think this caveat weakens the conclusions of this paper, it may impact the interpretation of future experiments that use these tools, and thus should be clearly discussed in the paper. Especially considering the authors argue that most disease variants of UBA5 are partial loss-of-functions, the amplification effect could potentially mask the phenotypes of milder hypomorphic alleles. If the authors could also show that the T2A-Gal4 expression pattern in the brain matches well with that of endogenous RNA or protein (e.g. using HCR-FISH or antibody), it would help to alleviate this concern.

We thank the reviewer for pointing out the issue.

Regarding the humanization strategy we used in the study, we agree that this is a binary system which could induce overexpression of the target protein. However, as the reviewer also points out, this temperature sensitive system also enables us to flexibly adjust the expression level of the target protein (PMIDs 34113007, 35348658, 36206744), which is especially useful to study partial LoF variants. In our study we have successfully compared the relevant allelic strength of most of the variants.

We agree with the reviewer that a masking effect may exist in our system due to its gene overexpression nature. However, we cannot conclude that this masking effect really affects the three Group IA variants in our tests. The three variants are mild LoF, which is supported by our biochemical assays. Individuals homozygous for one of the Group IA variants, p.A371T, do not have any obvious phenotype, which is also consistent with our findings in flies.

Regarding the expression pattern of the T2A-GAL4, the Bellen lab has generated T2A-GAL4 lines for more than 3,000 genes. The expression pattern of many GAL4 lines faithfully reflect the expression pattern of the endogenous genes, which has been shown in our previous publications (PMIDs 25824290, 29565247, 31674908).

Recommendations For The Authors:

As related to the expression pattern comment in the public review, I think the authors could also take advantage of Fly Cell Atlas or other available scRNA-seq atlases of the fly brain to present a much more detailed description of the Uba5 expression profile with minimal additional effort. If the cells that express it share other features or genes (other than the para that the authors mention), this could lead to further insights about the gene's neuronal or glial functions.

In response to the reviewer, we show the expression pattern of Uba5 documented in FlyCellAtlas and another adult brain single-cell RNA seq profile (PMID 29909982) in the revised manuscript.

In addition, one of the mutants (assuming the same one) is referred to as Leu254Pro in some parts of the manuscript while in some other parts (including tables 1-2) it is Lys254Pro.

We apologize for the mistakes. The variant should be Leu254Pro and we have made these corrections in the revised manuscript.

Reviewer #3

Summary:

Variants in the UBA5 gene are associated with rare developmental and epileptic encephalopathy, DEE44. This research developed a system to assess in vivo and in vitro genotype-phenotype relationships between UBA5 allele series by humanized UBA5 fly models and biochemical activity assays. This study provides a basis for evaluating current and future individuals afflicted with this rare disease.

Strengths:

The authors developed a method to measure the enzymatic reaction activity of UBA5 mutants over time by applying the UbiReal method, which can monitor each reaction step of ubiquitination in real time using fluorescence polarization. They also classified fruit fly carrying humanized UBA5 variants into groups based on phenotype. They found a correlation between biochemical UBA5 activity and phenotype severity.

Weaknesses:

In the case of human DEE44, compound heterozygotes with both loss-of-function and hypomorphic forms (e.g., p.Ala371Thr, p.Asp389Gly, p.Asp389Tyr) may cause disease states. The presented models have failed to evaluate such cases.

We agree with the reviewer that our current system has a limitation that it evaluates one variant at a time rather than any combination of variants. However, our biochemical data do show that the three Group IA variants are mild LoF variants rather than benign variants. One of these variants, p.A371T, does not cause any obvious phenotype in homozygous individuals, which is also consistent with our findings in flies. The modeling of variant combinations, especially the Group IA/Group III combinations could be carried out in future studies.

Recommendations For The Authors:

Figure 3G. Typo. "ContonS" should be replaced by "CantonS."

We apologize for the spelling mistake. We correct the typo in the revised manuscript.

Figure 5. The labels should be in uppercase instead of lowercase.

We correct the panel labels in the revised manuscript.

Figure 6A. Is the molecular weight of UBA5~UFM1 intermediate (99 kDa) in model Figure correct? In Fig. 6B, the molecular weight of UBA5~UFM1 intermediate seems to be 70-75 kDa.

Both are correct. The molecular weight depicted in the schematic of Figure 6A is based on the UBA5 dimer, which dissociates in the SDS-PAGE gel shown in Figure 6B. We have reconfigured the schematic to make this more apparent.

Figure. 6E, F, H, and I. The time points for quantification in these figures should be specified.

We apologize for the confusion. The details on data quantification are now more thoroughly explained in the Methods.

Brings to light that this is a hard concept to understand and singularly define, however, we shouldn't find the easy way out by just describing this as an illness in a dismissive way that doesn't get to the root of the issue.

Author Response

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

Editorial comments:

Comment 1 - Recommendations for the authors: please note that you control which revisions to undertake from the public reviews and recommendations for the authors.

We appreciate the feedback from the 3 Reviewers and Editor. We have enumerated each Reviewer comment and provide a detailed response. We endeavoured to include each suggestion into the revised manuscript. All changes in the manuscript are indicated in red font. In instances in which we respectfully disagree with the Reviewer, we have provided a fair rebuttal. We feel the comments from the Reviewers has significantly improved the clarity and quality of the manuscript.

Comment 2 - The revision process has demonstrated the value of your work, highlighting both its strengths and shortcomings. Importantly, it provides detailed and achievable suggestions for improving the current version of your contribution.

We thank the Reviewers and Editor for their time and expert input on our manuscript. We feel the suggestions from the Reviewers to address the shortcomings has resulted in a significantly improved manuscript.

Comment 3 - There is a general consensus among the reviewers on three key aspects. Firstly, the article would greatly benefit from a clearer layout of the experimental design and methodology, potentially including schematics to help readers comprehend the complexity and details of the study.

We appreciate the feedback from Reviewer 2 in particular. We have added a new schematic for Experiment 3 (see PUBLIC REVIEWS Reviewer #2 Comment 2). We have also revised the Results section by including subheadings and additional text to help explain the methods.

Comment 4 - Secondly, conducting a more comprehensive analysis of the available dataset, utilizing tools such as WGCNA to explore gene co-expression networks beyond specific genes, is recommended. Additionally, it is advised to exercise greater caution when discussing the limitations of the employed methods.

The suggestion for the WGCNA is excellent and very much appreciated. The revised manuscript includes WGCNA for both the MBH and pituitary gland. See Figures S3 & Table S6 and lines 166-182; 497-505).

Comment 5 - Thirdly, expanding the results section to create a more engaging narrative that guides readers through the numerous findings, and extending the discussion and conclusions to emphasize the ecological relevance of learning photoperiodic/seasonal responses and highlighting the presented model, would be valuable.

These were excellent suggestions that significantly improved the clarity and quality of the manuscript. The results section included several subheadings to help break up of the transitions across experiments. We have also significantly revised the introduction and discussion to include the ecological relevance and importance to consider sex as a factor in the interpretations.

Comment 6 - Finally, please pay close attention to the comment on the statistical analysis provided by Rev#2.

It is unclear why the Benjamini-Hochberg’s FDR analyses was suggested. The statistical test is a version of the Bonferroni test but is less stringent. We prefer to use conservative tests (i.e., Bonferroni correction). Moreover, the Bonferroni correction is the commonly used statistical tests in the field. To be consistent with the field and to be careful in our statistical approach, the revised manuscript did not change the post-hoc correction.

PUBLIC REVIEWS:

Reviewer #1:

Comment 1 - The authors investigated the molecular correlates in potential neural centers in the Japanese quail brain associated with photoperiod-induced life-history states. The authors simulated photoperiod to attain winter and summer-like physiology and samples of neural tissues at spring, and autumn life-history states, daily rhythms in transcripts in solstices and equinox, and lastly studies FSHb transcripts in the pituitary. The experiments are based on a series of changes in photoperiod and gave some interesting results. The experiment did not have a control for no change in photoperiod so it seems possible that endogenous rhythms could be another aspect of seasonal rhythms that lack in this study. The short-day group does not explain the endogenous seasonal response.

We thank the Reviewer for the fair assessment of the manuscript. The statement ‘the experiment did not have a control for no change in photoperiod’ is not clear to us. We think the Reviewer is arguing that prolonged constant photoperiod was not conducted to examine circannual timing in avian reproduction. The constant short photoperiod in Exp3 does provide the ability to examine the initial stages of interval timing. A different endogenous mechanism used by animals. The revised manuscript has clarified the different physiological responses.

Comment 2 - The manuscript would benefit from further clarity in synthesizing different sections. Additionally, there are some instances of unclear language and numerous typos throughout the manuscript. A thorough revision is recommended, including addressing sentence structure for improved clarity, reframing sentences where necessary, correcting typos, conducting a grammar check, and enhancing overall writing clarity.

We have incorporated the suggestions from both Reviewer 1 and Reviewer 2 that aimed to increase the clarity of the manuscript. We have provided detailed responses to each comment below and state how each comment was incorporated in the revised manuscript. We also had the manuscript reviewed by a colleague to help identify issues associated with sentence structure, grammar, and spelling.

Comment 3 - Data analysis needs more clarity particularly how transcriptome data explains different physiological measures across seasonal life-history states. It seems the discussion is built around a few genes that have been studied in other published literature on quail seasonal response. Extending results on the promotor of DEGs and building discussion is an extrapolating discussion on limited evidence and seems redundant.

A new statistical analysis (ie., WGCNA) was conducted to identify relations between photoperiod, physiology and transcripts. The focus on the few photoperiodic gene was kept in the discussion as the transcript expression is important to highlight the differences from the prevailing hypotheses and novel patterns of expression across seasonal timescales. See Figures S3 & Table S6 and lines 166-182; 497-505).

Comment 4 - Last, I wondered if it would be possible to add an ecological context for the frequent change in the photoperiod schedule and not take account of the endogenous annual response. Adding discussion on ecological relevance would make more sense.

This is an excellent suggestion. The introduction and discussion were substantially revised to include the ecological relevance.

Reviewer #2:

Comment 1 - This study is carefully designed and well executed, including a comprehensive suite of endpoint measures and large sample sizes that give confidence in the results. I have a few general comments and suggestions that the authors might find helpful.

We appreciate the Reviewers support for our manuscript. We have endeavoured to incorporate all suggestions in the revised manuscript.

Comment 2 - I found it difficult to fully grasp the experimental design, including the length of light treatment in the three different experiments (which appears to extend from 2 weeks up to 8 weeks). A graphical description of the experimental design along a timeline would be very helpful to the reader. I suggest adding the respective sample sizes to such a graphic, because this information is currently also difficult to keep track of.

We have created a new figure panel to address the Reviewer’s concern. See figure S4 panel ‘a’. The new schematic representation was designed to illustrate the similarity in experimental design used in Experiment 1 and Experiment 2. But clearly illustrates the extended short photoperiod manipulation (4 weeks and not 8 weeks). We added the sample sizes to initial drafts but felt the added text hindered the clarity of the schematic representation (particularly for Fig1a). The sample sizes for each experiment and treatment are provided in the raw data provided in the supplementary Table 1. For this reason, we have opted to not add the sample size to each diagram. We hope that the Reviewer will understand our perspective.

Comment 3 - The authors use a lot of terminology that is second nature to a chronobiologist but may be difficult for the general reader to keep track of. For example, what is the difference between "photoinducibility" and "photosensitivity"? Similarly, "vernal" and "autumnal" should be briefly explained at the outset, or maybe simply say "spring equinox" and "fall equinox."

This is a very helpful suggestion, and we thank the Reviewer. Two changes were made to the manuscript to address this comment. First, we revised the second introductory paragraph to describe the photoperiodic response and the terms used. Second, we have removed all reference to ‘vernal’ and replaced with ‘spring’. We opted to keep ‘autumn’ as the change to ‘fall’ did not provide the clarity of seasonal state in some statements (as fall is also used as a downward direction).

Comment 4 What was the rationale for using only male birds in this study? The authors may want to include a brief discussion on whether the expected results for females might be similar to or different from what they found in males, and why.

We agree with the Reviewer’s position that studies should include, or least describe, male and female biology. We have revised the text to address this comment. In the methods, we provide 2 sentences that state the photoperiodic response is the same for both male and females, and why males were selected. See lines (352-355). Then, in the discussion, we describe why females will be important to study how other supplementary environmental cues impact seasonal timing of reproduction. See lines (312-330; and 334-339).

Comment 5 - The authors used the Bonferroni correction method to account for multiple hypothesis testing of measures of testes mass, body mass, fat score, vimentin immunoreactivity and qPCR analyses in Study 1. I don't think Bonferroni is ever appropriate for biological data: these methods assume that all variables are independent of each other, an assumption that is almost never warranted in biology. In fact, the data show clear relationships between these endpoint measures. Alternatively, one might use Benjamini-Hochberg's FDR correction or various methods for calculating the corrected alpha level.

This concern is not clear to us. The Benjamini-Hochberg’s FDR is a slight modification of the Bonferroni correction. Moreover, the FDR is a less-stringent statistical test compared to the Bonferroni correction. We prefer to keep the Bonferroni approach to correct for multiple tests for two reasons. First, this test is commonly used in the field of chronobiology, and second, the Bonferroni correction is more conservative. We hope the Reviewer will appreciate our perspective to be consistent with the research field and higher stringency in our statistical approach.

Comment 6 - The graphical interpretations of the results shown in Figure 1n and Figure 3e, along with the hypothesized working model shown in Figure S5, might best be combined into a single figure that becomes part of the Discussion. As is, I do not think these interpretative graphics (which are well done and super helpful!) are appropriate for the Results section.

We appreciate the Reviewer’s suggestion. During the revision we developed a single figure to show the graphical representation for the respective experiments. Unfortunately, we found the single source to be very difficult to provide a clear description and overview of the findings. We feel that the interpretations, (admittedly unusual for Results section) are best placed in the respective figures that correspond to the different experiments.

Reviewer #3:

Comment 1a - It is well known that as seasonal day length increases, molecular cascades in the brain are triggered to ready an individual for reproduction. Some of these changes, however, can begin to occur before the day length threshold is reached, suggesting that short days similarly have the capacity to alter aspects of phenotype. This study seeks to understand the mechanisms by which short days can accomplish this task, which is an interesting and important question in the field of organismal biology and endocrinology.

We thank the Reviewer for their positive feedback.

Comment 1b - The set of studies that this manuscript presents is comprehensive and well-controlled. Many of the effects are also strong and thus offer tantalizing hints about the endo-molecular basis by which short days might stimulate major changes in body condition. Another strength is that the authors put together a compelling model for how different facets of an animal's reproductive state come "on line" as day length increases and spring approaches. In this way, I think the authors broadly fulfill their aims.

We thank the Reviewer for the positive support of our research and manuscript.

Comment 1c - I do, however, also think that there are a few weaknesses that the authors should consider, or that readers should consider when evaluating this manuscript. First, some of the molecular genetic analyses should be interpreted with greater caution. By bioinformatically showing that certain DNA motifs exist within a gene promoter (e.g., FSHbeta), one is not generating robust evidence that corresponding transcription factors actually regulate the expression of the gene in question. In fact, some may argue that this line of evidence only offers weak support for such a conclusion. I appreciate that actually running the laboratory experiments necessary to generate strong support for these types of conclusions is not trivial, and doing so may even be impossible. I would therefore suggest a clear admission of these limitations in the paper.

We agree with the Reviewer’s position. The transcription binding protein analyses was used as a means to identify potential factors involved in the regulation of transcript expression. We have written a new paragraph to address this comment. In the discussion, we that highlight the links between the well characterised circadian regulation of photoperiodic transcripts (e.g, D- & E-box elements and the photoperiodic control of TSHβ. We also indicate that our bioinformatic approach identified potentially new transcription binding motifs, and provide a clear admission and state that functional analyses are required to determine necessity of these pathways (e.g., MEF2). See lines 293-295.

Comment 2 - Second, I have another issue with the interpretation of data presented in Figure 3. The data show that FSHbeta increases in expression in the 8Lext group, suggesting that endogenous drivers likely act to increase the expression of this gene despite no change in day length. However, more robust effects are reported for FSHbeta expression in the 10v and 12v groups, even compared to the 8Lext group. Doesn't this suggest that both endogenous mechanisms and changes in day length work together to ramp up FSHbeta? The rest of the paper seemed to emphasize endogenous mechanisms and gloss over the fact that such mechanisms likely work additively with other factors. I felt like there was more nuance to these findings than the authors were getting into.

We agree with the Reviewer and a similar concern was raised by Reviewer 1. Our aim was to highlight that FSH expression increased in constant short photoperiod. We have revised the manuscript to address the concern raised by the Reviewer. We have added 2 sentences in the results to highlight the additive role of endogenous timing and photoperiodic effects on FSH expression (see lines 223-226). We have kept the text that describes endogenous increases in expression (e.g., FSH/GnRH) in response to short photoperiod in the manuscript as this observation is not influenced by long photoperiod.

Comment 3 - Third, studies 1 - 3 are well controlled; however, I'm left wondering how much of an effect the transitions in day length might have on the underlying molecular processes that mediate changes in body condition. While the changes in day length are themselves ecologically relevant, the transitions between day length states are not. How do we know, for example, that more gradual changes in day length that occur over long timespans do not produce different effects at the levels of the brain and body? This seemed especially relevant for study 3, where animals experience a rather sudden change in day length. I recognize that these experimental methods are well described in the literature, and they have been used by endocrinologists for a long time; nonetheless, I think questions remain.

There are two points raised in this comment. First, the effect of transition in day length on body condition. We are investigating the impact of photoperiodic transitions on body condition. The ongoing project has examined the changes in tissue lipid content and conducted transcriptomic analyses of multiple peripheral tissues involved in energy balance. Although we made an initial attempt to combine all the findings into a single manuscript, the large datasets resulted in an overwhelming manuscript that lacked clarity. Instead, we have opted for two manuscripts that focus on the respective physiological systems. Those data should be published shortly. We did expand the discussion by developing a single paragraph that focused on the pattern of POMC expression and changes in quail body mass and adipose tissue. See lines 300-311.

Second, the Reviewer raised the issue of more gradual changes in day length over longer timespans. The day length and duration of exposure selected was to replicate previously used photoperiod manipulations to ensure reproducibility in research programmes, and to reduce the impact of photoperiod history (see lines 367-369). The present manuscript is the first study in birds to examine multiple intervening (ie within the extreme long- and short-photoperiods) day length conditions and we feel this is a major and novel contribution to the field. We agree that other time points (e.g., 13L:11D), or quicker/longer timespans could provide additional insight into the molecular mechanisms that govern seasonal transitions in reproduction/energy balance. The question raised by the Reviewer requires the types of studies that use natural conditions from wild-caught animals (or semi-natural laboratory settings) and beyond the focus of the current manuscript.

Recommendations For The Authors:

Reviewer #1

Comment 1 - Abstract: Overall abstract needs more clarity in rationale, hypothesis, and result outcomes. How this study advances our knowledge in seasonal/ photoperiodic regulation of reproduction in birds. Particularly what knowledge gap FSHb results fill in.

We have substantially revised the abstract considering the Reviewer’s suggestions. The abstract has clarified the rationale, hypothesis and results outcomes. We have also added new introductory and concluding statements that place the work into a wider ecological context (as suggested below).

Comment 2 - In general the introduction needs more clarity and doesn't seem to cover the ecological relevance of learning photoperiodic/seasonal response.

We agree with the Reviewer the introduction could be improved. We have substantially revised the introduction with an aim to increase the clarity. This involved an addition on the ecological context, clarification of the photoperiodic states in birds, and a description of the general and specific objectives. Note we did not include an introduction to ‘learning’ of the photoperiodic response, as the term implies a cognitive component is involved which is incorrect. See lines (61-67, 71-74, 80-86, and 100-105).

Comment 3 - Line 58: What does the author mean by "future seasonal environment" Is it to introduce change in climate or future seasonal events? This sentence needs rephrasing and more clarity.

In response to Comment 2, we have revised the introductory paragraph and the sentence was removed from the text.

Comment 4 - Line 63: I would recommend the use of circannual rhythms with caution for the kind of experiments authors have proposed. The approach used here is beyond the scope of addressing circannual endogenous rhythms, which can be tested only independent of photoperiod change.

We agree with the Reviewer’s concern. The use of circannual rhythms was limited to the first paragraph (lines 56-63) only to introduce the concept of endogenous rhythmicity. We were careful to not use the term ‘circannual’ for the rest of the manuscript, as the Reviewer has indicated, would be inappropriate. We have retained the use of ‘endogenous program’ to refer to the molecular and physiological changes that can occur independent of photoperiod change (ie Experiment 3). In this case, the use of endogenous is appropriate as this form of timing adheres to an interval timer. We also provided a definition for interval timer and ecological examples to illustrate the difference between circannual rhythms and annual interval timer (see lines 71-74). We also reviewed the entire manuscript to ensure the distinction for the endogenous program was clear.

Comment 5 - Another aspect authors missed is that Quail is not an absolute photorefractory (Robinson and Follett, 1982).

We agree with the Reviewer that quail are not absolute photorefractory (but instead relative photorefractory). As our photoperiod manipulations do not address criterion 1, or criterion 2 of the avian photoperiodic response (MacDougall-Shackelton et al., 2009; see https://doi.org/10.1093/icb/icp048), we feel that adding the type of photorefractory response would be a distraction and reduce the clarity of the concepts/experimental design described in the manuscript.

Comment 6 - Line 223-234: "Chicks were raised under constant light and constant heat lamp". Constant photoperiod experienced during development raises concern on how this pretreatment would shape the adult seasonal response, which could be different in the seasonal response of birds raised in natural photoperiod. If this is correct, the results shown are not tenable for birds inhabiting the natural environment.

The light schedule used in our experiment is the most appropriate for laboratory reared chicks. The light schedule, use of an incubator and hatchery is commonly used in research laboratories. The procedure serves to increase the hatch rate and welfare of chicks. Undoubtedly there will be some early developmental programming effects on quail development. However, the gonadal response across all 3 experiments was consistent with the vast scientific literature on the avian photoperiodic response in both laboratory and wild birds. As the robust gonadal response clearly replicated previous studies, we are confident the results are tenable for birds inhabiting natural environments.

Comment 7 - Numerous studies done in mammals suggest that photoperiod experienced in the early life stage affects the circadian and seasonal response in adults (Ciarleglio et al., 2011, Perinatal photoperiod imprints the circadian clock, Nat Neurosceince; Stetson M., et al., 1986, Maternal transfer of photoperiodic information influences the photoperiodic response of prepubertal Djungarian hamsters).

We agree with the Reviewer that developmental programming in mammals is important for the photoperiodic response. However, there are vast differences between the avian and mammalian photoperiodic response. Critically, in mammals, the maternal transfer of information to the offspring is achieved via the melatonin hormone. Conversely, in birds, melatonin is not necessary, nor sufficient for photoperiodic time measurement (Juss et al., 1993; see https://doi.org/10.1098/rspb.1993.0121). It is not scientifically tenable to relate the mammalian and avian photoperiodic responses in adulthood based on early developmental programs. For this reason, we did not introduce or discuss developmental programming in our manuscript.

Comment 8 - Please give details on the month in which these birds were exposed to different short and long photoperiods. It is not clear in the method section. The birds experience long to short day transition and then back to long day in 16 weeks (~ 4 months). The annual cycle is ~12 months long in nature. Again, what is the ecological relevance of such an experimental paradigm. This could give some idea on photoperiodic response, but not on how the endogenous annual cycle would respond.

Birds were delivered in September 2019 and 2020. (We have added these details to the manuscript (see lines 351-352). We agree with the Reviewer that the ecological relevance of the experimental design is limited. Our focus was to use laboratory conditions and well characterised photoperiodic manipulations to examine the role of the environmental, initial predictive cue to time seasonal transitions in reproduction. The 2-week duration for each photoperiod state in Experiment 1 provides the ability to eliminate the impact of photoperiodic history (see lines 367-369; Stevenson et al., 2012a) and reduce the time necessary for the research project. As described above in Comment #4 – we did not examine the endogenous annual cycle – but instead focused on an endogenous interval timer. Experiment 3 was designed to best examine an endogenous interval timer.

Comment 9 - Line 251: "A jugular blood sample" Please rephrase this sentence and add 50 ul heparinized tubes

We thank the Reviewer for identifying this oversight. The text was changed accordingly.

Comment 10 - Line 259: The scale.....fat pads" - The sentence doesn't read correctly.

The sentence was revised accordingly.

Comment 11 - Line 274: Male.....six weeks. It is not clear from this sentence; what photoperiod birds were exposed to before transferring to 2 long days. Is it 16 or 14 LD.

The birds were held in 16L. The text has been revised accordingly.

Comment 12 - Line 276: It is not clear what is Home Office approved schedule 1. This may be a commonly used term for animal sacrifice protocol in UK and Europe. But it is not familiar jargon for the rest of the globe.

We apologise for the jargon. The text was revised to include the exact methods (decapitation followed by exsanguination).

Comment 13 - Line 277-284: Birds under SD for 4 weeks (8 Lext) is a bit confusing and particularly in the context of studying endogenous rhythm. Needs more clarity.

The text was revised to improve the clarity. The manuscript now states: ‘A subset of birds (n=6) was maintained in short day photoperiods for four more weeks (8Lext). This group of birds provided the ability to examine whether an endogenous increase in FSHβ expression would occur in constant short day photoperiod condition.’

Comment 14 - Line 322-323: Give RIN number (RNA integrity number) here which is a very common parameter to determine RNA degradation in RNAseq experiments. I guess, the MiniON is a portable sequencer and sequences one sample at a time. If this is true authors should consider any batch effect in sequencing and use it as a covariate in the model.

The RIN values from our extraction protocol reliably produce RIN values >9.0. The text now states: Isolated RNA reliably has RIN values >9.0 for both the mediobasal hypothalamus and pituitary gland. Our RIN values are well above the recommended 7.0 limit. The Reviewer is correct that MinION is portable, however, more than one sample can be run at a time. We stated in the text (lines 454-460) that birds were counterbalanced across Flow cells so that each sequencing run had 9 samples, one from each treatment group. Our counterbalancing approach and quality control steps prevented batch effects.

Comment 15 - Line 397-398: Adding quail or chicken-specific vimentin peptide pre-incubation with primary Ab will serve more confirming control. Omitting primary Ab doesn't address cross-reactive/ nonspecific binding issues.

We agree that a positive control (ie primary Ab) is the gold standard to support specificity of the antibody. Unfortunately, we have not found a supplier of the epitope for quail/chicken vimentin. We have conducted another in silico analysis an established that the sequences for the vimentin antibody is specific for vimentin. The next closest sequence alignment is only 68% for a protein that is not expressed in the brain. The immunoreactive pattern observed in our histology reproduces work from mammalian models in which the epitope is available. Therefore, we are confident that our immunoreactive signal for vimentin is specific. We have added the in silico analysis in the manuscript on lines 535-538.

Comment 16 - Line 430: Was the GLM model used for testing all variables? Running a statistical model to explain Differentially expressed genes, photoperiod, and physiological variables together will give a more conclusive outcome to explain the photoperiod effect and seasonal state.

A similar comment was raised by Reviewer 2. We have conducted a WGCNA analyses to examine the relationship between photoperiod, physiological variables and DEG. See Figures S3 & Table S6 and lines 166-182; 497-505).

Comment 17 - It is a bit unclear why the author used cherry-picking approach by talking about only a few genes that have been studied as key regulators of photoperiodic response in quail. What was the purpose of transcriptome? A better approach would have been to use a model to reduce the data (PCA) and explain the physiological response by regression against different PCs.

We agree with the Reviewer that other statistical approaches could be conducted, and other genes could be discussed. However, we focussed on the key regulators of the photoperiodic response in quail as these are the well characterised genes. It is important that our discussion focused on these transcripts as most do not conform to the predicted patterns of expression. We feel it is best that we keep the focus on these genes.

Comment 18 - TSHb result is inconsistent with past studies, where TSHb is the first responder gene on photoinduction. The author did not pay attention to explaining it further in the discussion.

We respectfully disagree with the Reviewer. Our results are consistent with past studies and show that TSHβ expression is a molecular marker of long day photoperiod. Our study does not examine photoinduction; which does not provide the ability to compare between our study and previous work (eg., Nakao et al., 2008; see doi: 10.1038/nature06738). We have revised the text in consideration of the concern raised by the Reviewer. The text now states ‘Previous reports established that TSHβ expression is significantly increased during the period of photoinducibility in quail (Nakao et al., 2008). Although the present study did not directly examine photoinduction, TSHβ expression was consistently elevated in long day photoperiod (i.e., 16L).’. (see lines 262-265).

Comment 19 - PRL result seems interesting and there could be more discussion in relation to the rise in PRL transcripts levels termination of breeding. Elaborating on PRL expression and breeding termination can add more information to the discussion.

This comment is not clear to us, and we would incorporate a clarified comment in a revised manuscript. The increased expression of prolactin does not occur during the termination of breeding. The increase in prolactin occurs during the vernal increase in photoperiod (ie 14L) but does not have a clear link with gonadal growth.

Comment 20 - Line 217-219: Based......respectively. Sounds like a big claim with less evidence.

We have removed the sentence from the discussion.

Comment 21 - Line 220-223: The .....Bird. The sentence is not clear about how this study would add to ecological studies. Need more clarity on the importance of such data.

The sentence was removed from the text.

Comment 22 - I think that it would be helpful to add a couple of caveats to provide more ecological context. First, the model is only based on males, and responses in females could be different.

We agree with the Reviewer there are undoubtedly sex differences in timing seasonal biology. However, the photoperiodic response (growth and regression) is similar in both males and females. Sex differences exist in response to supplementary environmental cues (e.g., temperature). Males were used in these studies as the gonadal response to changes in photoperiod manipulations are much larger compared to ovarian changes in females. The focus on males allows for fewer animals to be used in the experiments and greater statistical power. To address the Reviewers concern, we have added a paragraph in the discussion that describes the similarity in photoperiodic responses in males and females, and the importance of supplementary cues for full reproductive development in female birds. We also provide a couple sentences in the methods that describe the justification for only males in the present study. See lines (Methods 352-355; Discussion 312-330; and 334-339).

Comment 23 - Last, I wondered if it would be possible to add an ecological context for the frequent change in the photoperiod schedule and not take account of the endogenous annual response. Would the procedure simulate a similar kind of underlined molecular response for a bird under natural conditions responding to changing daylight cycles on an annual time frame?

The discussion was considerably revised to address the ecological relevance of the study, and findings. We have added a sentence at the beginning of the discussion to highlight that the laboratory-based approach and photoperiodic manipulations reliable replicate previous findings using semi-natural conditions (Robinson and Follett, 1982) (See lines 248-250). We have already reduced the focus on the endogenous annual response.

Reviewer #2:

Comment 1 - The writing is very terse and could benefit from a more narrating style, which would make it a lot easier for the reader to get through some of the very data-heavy text. Breaking up the Results with subheadings would also be helpful.

We appreciate the suggestion to add subheadings to the Results. We added 3 descriptive headings for each other studies conducted in the manuscript. We feel the added revision (e.g., ecological) has improved the narrative and made the manuscript accessible to the wider readership.

Comment 2 - The transcriptome analyses could be developed a bit more. First, using the limma package would allow the authors to apply a more complete model to the DEG analyses, which would likely be superior to EdgeR. Second, the authors may want to consider WGCNA or a similar approach to discover gene co-expression modules, and then examine whether any of the resulting module eigengenes co-vary with any morphological or physiological measures and/or vary rhythmically.

This is an excellent suggestion, and the new analyses was incorporated into the revised manuscript. Using the Langfelder and Horvath 2008 WCGNA package we conducted module-trait analyses to examine co-variation in our findings. These data are presented in Figure S# and lines 476-484. We agree that other DEG analyses would be useful; our main objectives was to use BioDare2.0 to identify rhythmic transcription in the seasonal transcriptomes. EdgR provides an excellent approach to identify transcripts and commonly used.

Comment 3 - In the Data and code availability statement (lines 226ff) the authors state that "all raw data are available in Extended data Table 1." However, they should be submitted to the GEO database or a similar public repository along with all relevant metadata. Also, and maybe I overlooked this, I did not see anywhere that the "R code used in Study 1 is freely available" (I was not sure what "the methods reference list" was supposed to refer to). Instead of stating that "the full R code used is available upon request" I suggest making all scripts available via GitHub or Dataverse, along with all non-omics data. The advantage of the latter platform is that a citable DOI is assigned to each upload.

The data are now available in the GEO database and can be accessed see GSE241775. We have added this information to the text. The R code is now provided as a Table S11 so that the reader can directly access the script.

Comment 4 - Line 191: Delete the extra "that"

We thank the Reviewer for identifying the oversight. We have revised the text accordingly.

Comment 5 - Line 24f: What does "pseudo-randomly" mean? Maybe "haphazardly" would be more appropriate here?

The term pseudo-randomly is used to describe the organized manner in which subjects are assigned to each treatment group. The aim is to ensure that a particular physiological variable, such as body mass, is evenly distributed across treatment groups. (Note although the term derived from the field of psychology). The aim is to reduce bias in the experiment due to an initial bias established when assigning treatment group. We are reluctant to replace pseudorandomly with haphazardly as the latter does not imply a logical organization. We have added text to help clarify the reason. The text now state: At the end of each photoperiodic treatment a subset of quail (n=12) body mass was used as a measure to pseudo randomly select birds for tissue collection and served to reduce the potential for unintentional bias.

Comment 6 - Figure 1e,j: The text indicates that 398 and 130 genes were "rhythmically expressed" in the MBH and pituitary, respectively, but considerably fewer genes are shown in the heatmaps in Figure 1e,j. How were these genes selected, and what was the rationale for doing so? Also, some autumnal and vernal expression patterns show some strong similarities (e.g., 16a and 16v in the MBH), which could be discussed. Consider showing the two heatmaps with the columns also hierarchically clustered in a supplementary figure.

We agree with the Reviewer that the full heatmap for the transcripts should be provided. The heat maps in Figure 1 are based on the transcripts with the most significant change; and were selected to provide a graphical representation that would be easily digested by the wide readership. We have created a new figure (ie. Fig. S1) that provides all the transcripts in heat maps for both the MBH and pituitary gland.

Reviewer #3:

Comment 1 I do not have too much to add to this section of my review. Broadly speaking, I would suggest that the authors address some of the concerns I highlight above, and integrate their thoughts into the paper more than they currently do. I think this is particularly important with respect to the limitations of many of the bioinformatic analyses.

We thank the reviewer for their input and time assessing the manuscript. We have revised the manuscript in many sections incorporating the suggestions by Reviewer 3 above, and Reviewers 1 and 2.

Comment 2 Some of the methods are also a little scant. For example, the qPCR analyses are not described in sufficient detail to replicate the study. What are the efficiencies? Were samples run in duplicate? What was the housekeeping control gene used? Was there only one, or were multiple housekeeping genes used?

We apologise for the oversight, the absence of information was a mistake that missed our previous early revisions. The revised manuscript includes all the requested information. Line 333 states that all samples were run in duplicate. The efficiency for each transcript was within the MIQE guidelines (indicated on line 342) and were within the 0.7 to 1.0 range. Actin and glyceraldehyde 3-phosphate dehydrogenase were used as the reference transcripts. The most stable reference transcript was used to calculate fold change in target gene expression (lines 343-345).

Author Response

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

eLife assessment

In this important paper, the authors report a link between brumation and tissue size in frogs, summarizing convincing evidence that extended brumation is associated with smaller brain size and increased investment in reproduction-related tissues. The research will be of broad interest to ecologists, evolutionary biologists, and those interested in global change biology. While the dataset involves significant field work and advanced statistical analyses, the manuscript would benefit from more explanation of the models, including why frogs are a good model in which to address these questions, and from general improvement in the structure and conciseness.

We highly appreciate your positive assessment and that you considered our paper important and convincing.

Reviewer #1 (Public Review):

The authors have conducted lots of field work, lab work and statistical analysis to explore the effect of brumation on individual tissue investments, the evolutionary links between the relative costly tissue sizes, and the complex non-dependent processes of brain and reproductive evolution in anuran. The topic fits well within the scope of the journal and the manuscript is generally written well. The different parameters used in the present study will attract a board readership across ecology, zoology, evolution biology, and global change biology.

Thank you for your positive and supporting feedback.

Reviewer #2 (Public Review):

The authors set out to show how hibernation is linked to brain size in frogs. If there were broader aims it is hard to decipher them. The authors present an extremely impressive dataset and a thorough set of cutting-edge analyses. However not all details are well explained. The main result about hibernation and brain size is fairly convincing, but it is hard to think of broader implications for this study. Overall, the manuscript is very confusing and hard to follow.

Thank you for your compliments on our paper. As for your concerns, we have greatly revised our paper and, as we hope, improved its clarity. We have also added a few sentences to the conclusions to draw attention to potentially broader implications. Specifically, we describe how the focal traits of our study may all be affected by climate change. Differential constraints in necessary investments could be one of several reasons for the varying resilience to climate change between species in the same habitat.

Reviewer #1 (Recommendations For The Authors):

There are no issues on the availability of data and code.

Thank you.

Line 15: in the author contribution section, it seems that C.L.M. and J.P.Y are not in the author list.

These two authors are not part of this study. This was a mistake.

Line 24: I don't think it is vital or logical to address or compare too much on birds or mammals, which are not the focused taxa of the present study. Instead, it is better to clarify the reason why frogs and toads are ideal model taxon to this study.

The reason for comparisons with birds and mammals was that all hypotheses related to the various trade-offs tested here had been developed in these taxa. One of the points of our paper was that these needed validation beyond the two taxa, in addition to being tested against one another (each prediction had been developed in a specific group and typically in isolation of all other hypotheses).

Line 25-26: as the authors are shooting for eLife, as a general journal, it is not essential to provide the detailed methods in the abstract. But I think the authors need to strengthen the novelty of the work in the field here.

The strength of our study was that all traits were measured directly in our species, including estimates of hibernation duration. Prior studies used various proxies, categorial classification or datasets assembled from multiple sources. To us, this seemed like a sufficiently important advance in the field to mention it, but considering the reviewer’s comment, we have now removed it.

Line 28: "protracted brumation reduces brain size and instead promotes reproductive investments", as a correlative study, it is much more precise to change this sentence to a similar description as "protracted brumation is negatively correlated with brain size but is positively correlated with reproductive investments" here and related statements throughout the whole text.

We agree that, strictly speaking, a path analysis can only point toward possible causality and not provide hard evidence as experimental manipulation might. The wording may have been a bit too strong here in our attempt to minimize wordiness and because all our analyses combined very strongly pointed in this direction. However, we have now changed this as suggested even though it now reads almost as if we had done no more than conducting a simple correlation. We have further paid attention to the wording of our interpretations throughout the paper.

Line 32-33: it needs a bigger ending linking your main findings with the implication in understanding species response to the sustained environment change.

We have reworded the ending of the abstract to: “Our results provide novel insights into resource allocation strategies and possible constraints in trait diversification, which may have important implications for the adaptability of species under sustained environmental change.”

Line 63-68: this sentence is too long to understand and please simplify it.

We have split the sentence into two sentences.

Line 125-130: it is known that there are various frog reproductive modes (Crump et al. 2015) such as trade-offs between clutch size and egg size, different number of breeding during one year, etc. These different reproductive forms may also influence the brain size evolution with food availability and seasonal variations. Please clarify it.

Yes, anurans do have varying reproductive modes, but to us, there is no a priori reason to assume that such variation would have a direct effect on brain evolution. Rather, in our opinion, different reproductive modes would have indirect effects by affecting the environment in which reproduction occurs. For example, larvae developing under different environmental conditions (substrate, larval density, egg provisioning etc.) might affect developmental trajectories that could influence how resources are available and allocated to different organs, including the brain. Alternatively, reproductive modes could influence the choice of environment for reproduction, thereby possibly affecting mating strategies and ultimately trait investments associated with these strategies. Given we were asked to shorten our paper, we believe that ‘environmental effects’ remains broad enough to encompass such variation, thereby not necessitating disentangling the different, and likely primarily indirect, ways that reproductive modes could be linked to brain evolution. However, if the reviewer would find it important to go into such detail in the paper, we will be happy to do so.

Line 186-187: it is necessary to mention here that the authors also conducted sensitivity analyses to apply 2{degree sign}C or 4{degree sign}C below their experimentally derived as thresholds to test the robustness of the results to data uncertainty.

We have added “(details on methodology and various sensitivity analyses for validation in Material and Methods)” to indicate the different types of sensitivity analyses, which included more than simply 2 or 4°C difference.

Line 188: please change "In phylogenetic regressions" to "after controlling for phylogenetic autocorrelation/pseudo-replication" or similar sentence here.

Our focus here was the phylogenetically informed GLS model rather than phylogenetic control itself. In the latter case, it would still not be clear what type of model was conducted with such phylogenetic control. To avoid any shorthand, we have reworded for more precision: “We employed phylogenetic generalized least-squares (PGLS) models, …”