to manufacture more anxiety in the form of buildings

Author Response:

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

Reviewer #1 (Public Review):

This revised manuscript by Walker et. al. addresses some of the editorial points and conceptual discussion, but in general, most of my suggestions (as the previous reviewer #1) for additional experimentation or addition were not addressed as discussed below. Therefore, my overall review has not changed.

In our previous response, we included i) extra experimental data illustrating the reproducibility of our results and ii) added transcription start site data at the request of this reviewer. We included the information because we agreed with the reviewer that these were important points to address. For the points raised again below, we explained why the additional analysis was unlikely to add much in terms of insight or rigour. We have elaborated further below.   

1) For example, in point 1, the suggested analysis was not performed because it is not trivial. My reason for making this suggestion is that the original manuscript was limited to Vibrio cholerae, and the impact of the manuscript would increase if the findings here were demonstrated to be more broadly applicable. I expect papers published in eLife to have such broad applicability. But no changes were made to the manuscript in this regard. The revised version is still limited to only Vibrio cholerae.

Our paper is focused on the unexpected co-operative interactions between HapR and CRP. Such co-binding of two transcription factors to the same DNA site is unexpected. Consequently, it is this mode of DNA binding that is likely to be of broad interest. With this in mind, we did provide experimental, and bioinformatic, analyses for other regulatory regions and other vibrio species (Figures S3 and S6). This, in our view, is where the “broad applicability” for papers published in eLife comes from.

The analysis the reviewer suggests is not related to the main message of our paper. Instead, the reviewer is asking how many HapR binding sites seen here by ChIP-seq are also seen in other vibrio species by ChIP-seq. This is only likely to be of interest to readers with an extremely specific interest in both vibrio species and HapR. The reviewer states above that we did not make the change “because it is not trivial”. This is an oversimplification of the rationale we presented in our response. The analysis is indeed not straightforward. However, much more importantly, the outcome is unlikely to be of interest to many readers, and has no bearing on the rigour of work. With this in mind, we do not think our position is unreasonable. We also stress that, should a reader with this very specific interest want to explore further, all of our data are freely available for them to do so.

2) For point 2, the activity of FLAG-tag luxO could have been simply validated in a complementation assay. Yes, they demonstrated DNA binding, but that is not the only activity of LuxO.

DNA binding by LuxO is the only activity of the protein with which we are concerned in our paper. Furthermore, LuxO is very much a side issue; we found binding to only the known targets and potentially, at very low levels, one additional target. No further LuxO experiments were done for this reason. Indeed, even if these data were removed completely, our conclusions would not change or be supported any less vigorously. We are happy to remove the LuxO data if the reviewer would prefer but this would seem like overkill.

3) For point 7, the transcriptional fusions were not explored at different times or different media, which is also something that was hinted at by other reviewers. In regard to exploring expression at different time points, this seems particularly relevant for QS regulated genes.

In their previous review, the reviewer did not request that such experiments were done. Similarly, no other reviewer requested these experiments. Instead, this reviewer i) commented that lacZ fusions were not as sensitive as luciferase fusions ii) asked if we had done any time point experiments. We agreed with the first point, whilst also noting that lacZ is not unusual to use as a reporter. For the second point, we responded that we had not done such experiments (which by the reviewer’s own logic would have been complicated using lacZ as a reporter). This seems like a perfectly reasonable way to respond.   

We should stress that these comments all refer to Figure 2a, which was our initial screening of 23 promoter::lacZ fusions, supported by separate in vitro transcription assays. Only one of these fusions was followed up as the main story in the paper. Given that the other 22 fusions were not investigated further, and do not form part of the main story, there would seem little value in now going back to assay them at different time points.

4) For point 13, the authors express that doing an additional CHIP-Seq is outside of the scope of this manuscript. Perhaps that is the case, but the point of the comment is to validate the in vitro binding results with an in vivo binding assay. A targeted CHIP-Seq approach specifically analyzing the promoters where cooperative binding was observed in vitro could have addressed this point.

We did appreciate the original comment, and responded as such, but we do think additional ChIP-seq assays are outside the scope of this paper.

Reviewer #2 (Public Review):

This manuscript by Walker et al describes an elegant study that synergizes our knowledge of virulence gene regulation of Vibrio cholerae. The work brings a new element of regulation for CRP, notably that CRP and the high density regulator HapR co-occupy the same site on the DNA but modeling predicts they occupy different faces of the DNA. The DNA binding and structural modeling work is nicely conducted and data of co-occupation are convincing. The work seeks to integrate the findings into our current state of knowledge of HapR and CRP regulated genes at the transition from the environment and infection. The strength of the paper is the nice ChIP-seq analysis and the structural modeling and the integration of their work with other studies.

We thank the reviewer for the positive comments.

The weakness is that it is not clear how representative these data are of multiple hapR/CRP binding sites

This comment does not consider all data in our paper. We did test our model experimentally at multiple HapR and CRP binding sites. These data are shown in Figure S6 and confirm the co-operative interaction between HapR and CRP at 4 of a further 5 shared binding sites tested. We also used bioinformatics to show the same juxtaposition of CRP and HapR sites in other vibrio species (Figure S3). Hence, the model seems representative of most sites shared by HapR and CRP.

or how the work integrates as a whole with the entire transcriptome that would include genes discovered by others.

At the request of the reviewers, our revision integrated our ChIP-seq data with dRNA-seq data. No other suggestions to ingrate transcriptome data were made by the reviewers. 

Overall this is a solid work that provides an understanding of integrated gene regulation in response to multiple environmental cues.

We thank the reviewer for the positive comment.

—————

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

Reviewer #1 (Public Review):

This manuscript by Walker et. al. explores the interplay between the global regulators HapR (the QS master high cell density (HDC) regulator) and CRP. Using ChIP-Seq, the authors find that at several sites, the HapR and CRP binding sites overlap. A detailed exploration of the murPQ promoter finds that CRP binding promotes HapR binding, which leads to repression of murPQ. The authors have a comprehensive set of experiments that paints a nice story providing a mechanistic explanation for converging global regulation.

We thank the reviewer for their positive evaluation.

I did feel there are some weak points though, in particular the lack of integration of previously identified transcription start sites

For completeness, we have now added the position and orientation or the nearest TSSs to each HapR or LuxO binding peak in Table 1 (based on Papenfort et al.).

the lack of replication (at least replication presented in the manuscript) for many figures,

We assume that the reviewer is referring to gel images rather than any other type of assay output (were error bars, derived from replicates, are shown). As is standard, we show representative gel images. All associated DNA binding and in vitro transcription experiments have been done multiple times. Indeed, comparison between figures reveals several instances of such replication (e.g. Figures 4b & 5d, Figures 4d & 5e). We have added details of repeats done to the methods section.

some oddities in the growth curve

We do not know why cells lacking hapR have a growth curve that appears biphasic. We can only assume that this is due to some regulatory effect of HapR, distinct from the murQP locus. Despite the unusual shape of the growth curve, the data are consistent with our conclusions.

and not reexamining their HapR/CRP cooperative binding model in vivo using ChIP-Seq.

We agree that these would be interesting experiments and, in the future, we may well do such work. Even without these data, our current model is well supported by the data presented (and the reviewer seems to agree with this above).

Reviewer #2 (Public Review):

This manuscript by Walker et al describes an elegant study that synergizes our knowledge of virulence gene regulation of Vibrio cholerae. The work brings a new element of regulation for CRP, notably that CRP and the high density regulator HapR co-occupy the same site on the DNA but modeling predicts they occupy different faces of the DNA. The DNA binding and structural modeling work is nicely conducted and data of co-occupation are convincing. The work could benefit from doing a better job in the manuscript preparation to integrate the findings into our current state of knowledge of HapR and CRP regulated genes and to elevate the impact of the work to address how bacteria are responding to the nutritional environment. Importantly, the focus of the work is heavily based on the impact of use of GlcNAc as a carbon source when bacteria bind to chitin in the environment, but absent the impact during infection when CRP and HapR have known roles. Further, the impact on biological events controlled by HapR integration with the utilization of carbon sources (including biofilm formation) is not explored.

We thank the reviewer for their overall positive evaluation.

The rigor and reproducibility of the work needs to be better conveyed.

Reviewer 1 made a similar comment (see above) and we have modified the manuscript accordingly.

Specific comments to address:

1)  Abstract. A comment on the impact of this work should be included in the last sentence. Specifically, how the integration of CRP with QS for gene expression under specific environments impacts the lifestyle of Vc is needed. The discussion includes comments regarding the impact of CRP regulation as a sensor of carbon source and nutrition and these could be quickly summarized as part of the abstract.

We have added an extra sentence. However, we have used cautious language as we do not show impacts on lifestyle (beyond MurNAc utilisation) directly. These can only be inferred.

2)  Line 74. This paper examines the overlap of HapR with CRP, but ignores entirely AphA. HapR is repressed by Qrrs (downstream of LuxO-P) while AphA is activated by Qrrs. With LuxO activating AphA, it has a significant sized "regulon" of genes turned on at low density. It seems reasonable that there is a possibility of overlap also between CRP and AphA. While doing an AphA CHIP-seq is likely outside the scope of this work, some bioinformatic or simply a visual analysis of the promoters known AphA regulated genes would be interest to comment on with speculation in the discussion and/or supplement.

In short, everything that the reviewer suggests here has already been done and was covered in our original submission (see text towards the end of the Discussion). Also, we would like to point the referee to our earlier publication (Haycocks et al. 2019. The quorum sensing transcription factor AphA directly regulates natural competence in Vibrio cholerae. PLoS Genet. 15:e1008362).

3)  Line 100. Accordingly with the above statement, the focus here on HapR indicates that the focus is on gene expression via LuxO and HapR, at high density. Thus the sentence should read "we sought to map the binding of LuxO and HapR of V. cholerae genome at high density".

Note that expression of LuxO and HapR is ectopic in these experiments (i.e. uncoupled from culture density).

4)  Line 109. The identification of minor LuxO binding site in the intergenic region between VC1142 and VC1143 raises whether there may be a previously unrecognized sRNA here. As another panel in figure S1, can you provide a map of the intergenic region showing the start codons and putative -10 to -35 sites. Is there room here for an sRNA? Is there one known from the many sRNA predictions / identifications previously done? Some additional analysis would be helpful.

We have added an extra panel to Figure S1 showing the position of TSSs relative to the location of LuxO binding. We have altered the main text to accommodate this addition..

5)  Line 117. This sentence states that the CHIP seq analysis in this study includes previously identified HapR regulated genes, but does not reveal that many known HapR regulated genes are absent from Table 1 and thus were missed in this study. Of 24 HapR regulated investigated by Tsou et al, only 1 is found in Table 1 of this study. A few are commented in the discussion and Figure S7. It might be useful to add a Venn Diagram to Figure 1 (and list table in supplement) for results of Tsou et al, Waters et al, Lin et al, and Nielson et al and any others). A major question is whether the trend found here for genes identified by CHIP-seq in this study hold up across the entire HapR regulon. There should also be comments in the discussion on perhaps how different methods (including growth state and carbon sources of media) may have impacted the complexity of the regulon identified by the different authors and different methods.

We have added a list of known sites to the supplementary material (new Table S1). We were unsure what was meant by the comment “A major question is whether the trend found here for genes identified by CHIP-seq in this study hold up across the entire HapR regulon”. We have added the extra comment to the discussion re growth conditions, also noting that most previous studies relied on in vitro, rather than in vivo, DNA binding assays.

6)  The transcription data are generally well performed. In all figures, add comments to the figure legends that the experiments are representative gels from n=# (the number of replicate experiments for the gel based assays). Statements to the rigor of the work are currently missing.

See responses above. We have added a comment on numbers of repeats to the methods section.

7)  Line 357-360. The demonstration of lack of growth on MurNAc is a nice for the impact of the work. However, more detailed comments are needed for M9 plus glucose for the uninformed reader to be reminded that growth in glucose is also impaired due to lack of cAMP in glucose replete conditions and thus minimal CRP is active. But why is this now dependent of hapR? A reminder also that in LB oligopeptides from tryptone are the main carbon source and thus CRP would be active.

We find this point a little confusing and, maybe, two issues (murQP regulation, and growth in general) are being conflated. In particular, we do not understand the comment “growth in glucose is also impaired due to lack of cAMP in glucose replete conditions and thus minimal CRP is active”.

Growth in glucose should indeed result in lower cAMP levels*, and hence less active CRP, but this does not impair growth. This is simply the cell’s strategy for using its preferred carbon source. If the reviewer were instead referring to some aspect of P_murQP_ regulation then yes, we would expect promoter activity to be lower because less active CRP would be available in the presence of glucose. The reviewer also comments “why is this now dependent of hapR?”. We assume that they are referring to some aspect of growth in minimal media with glucose. If so, the only hapR effect is the change in growth rate as cells enter mid-late log-phase (i.e. the growth curve looks somewhat biphasic). A similar effect is seen in all conditions. We do not know why this happens and can only conclude this is due to some unknown regulatory activity of HapR. Overall, the key point from these experiments is that loss if luxO, which results in constitutive hapR expression, lengthens lag phase only for growth with MurNAc as the sole carbon source.

*Although in V. fischeri (PMID: 26062003) cAMP levels increase in the presence of glucose.

8)  A great final experiment to demonstrate the model would have been to show co-localization of the promoter by CRP and HapR from bacteria grown in LB media but not in LB+glucose or in M9+glycerol and M9+MurNAc but not M9+glucose. This would enhance the model by linking more directly to the carbon sources (currently only indirect via growth curves)

This is unlikely to be as straightforward as suggested. The sensitivity of CRP binding to growth conditions is not uniform across different binding sites. For instance, the CRP dependence of the E. coli melAB promoter is only evident in minimal media (PMID: 11742992) whilst the role of CRP at the acs promoter is evident in tryptone broth (PMID: 14651625). Similarly, as noted above, in Vibrio fischeri glucose causes and increase in cAMP levels. (PMID: 26062003).

9) Discussion. Comments and model focus heavily on GlcNAc-6P but HapR has a regulator role also during late infection (high density). How does CRP co-operativity impact during the in vivo conditions?

We really can’t answer this question with any certainty; we have not done any infection experiments in this work.

Does the Biphasic role of CRP play a role here (PMID: 20862321)?

Again, we cannot answer this question with any confidence as experimentation would be required. However, the suggestion is certainly plausible.

Reviewer #3 (Public Review):

Bacteria sense and respond to multiple signals and cues to regulate gene expression. To define the complex network of signaling that ultimately controls transcription of many genes in cells requires an understanding of how multiple signaling systems can converge to effect gene expression and ensuing bacterial behaviors. The global transcription factor CRP has been studied for decades as a regulator of genes in response to glucose availability. It's direct and indirect effects on gene expression have been documented in E. coli and other bacteria including pathogens including Vibrio cholerae. Likewise, the master regulator of quorum sensing (QS), HapR), is a well-studied transcription factor that directly controls many genes in Vibrio cholerae and other Vibrios in response to autoinducer molecules that accumulate at high cell density. By contrast, low cell density gene expression is governed by another regulator AphA. It has not yet been described how HapR and CRP may together work to directly control transcription and what genes are under such direct dual control.

We thank the reviewer for their assessment of our work.

Using both in vivo methods with gene fusions to lacZ and in vitro transcription assays, the authors proceed to identify the smaller subset of genes whose transcription is directly repressed (7) and activated (2) by HapR. Prior work from this group identified the direct CRP binding sites in the V. cholerae genome as well as promoters with overlapping binding sites for AphA and CRP, thus it appears a logical extension of these prior studies is to explore here promoters for potential integration of HapR and CRP. Inclusion of this rationale was not included in the introduction of CRP protein to the in vitro experiments.

We understand the reviewer’s comment. However, the rationale for adding CRP was not that we had previously seen interplay between AphA and CRP (although this is a relevant discussion point, which we did make). Rather, we had noticed that there was an almost perfect CRP site perfectly positioned to activate PmurQP. Hence, CRP was added.

Seven genes are found to be repressed by HapR in vivo, the promoter regions of only six are repressed in vitro with purified HapR protein alone. The authors propose and then present evidence that the seventh promoter, which controls murPQ, requires CRP to be repressed by HapR both using in vivo and vitro methods. This is a critical insight that drives the rest of the manuscripts focus. The DNase protection assay conducted supports the emerging model that both CRP and HapR bind at the same region of the murPQ promoter, but interpret is difficult due to the poor quality of the blot.

There are areas of apparent protection at positions +1 to +15 that are not discussed, and the areas highlighted are difficult to observe with the blot provided.

We disagree on this point. The region between +1 and +15 is inherently resistant to attack by DNAseI and there are only ever very weak bands in this region (lane 1). Other than seeing small fluctuations in overall lane intensity (e.g. lanes 7-12 have a slightly lower signal throughout) the +1 to +15 banding pattern does not change. Conversely, there are dramatic changes in the banding pattern between around -30 and -60 (again, compare lane 1 to all other lanes). That CRP and HapR bind the same region is extremely clear. Also note that this is backed up by mutagenesis of the shared binding site (Figure 4c).

The model proposed at the end of the manuscript proposes physiological changes in cells that occur at transitions from the low to high cell density. Experiments in the paper that could strengthen this argument are incomplete. For example, in Fig. 4e it is unclear at what cell density the experiment is conducted.

Such details have been added to the figure legends and methods section.

The results with the wild type strain are intermediate relative to the other strains tested.

This is correct, and exactly what we would expect to see based on our model.

Cell density should affect the result here since HapR is produced at high density but not low density. This experiment would provide important additional insights supporting their model, by measuring activity at both cell densities and also in a luxO mutant locked at the high cell density. Conducting this experiment in conditions lacking and containing glucose would also reveal whether high glucose conditions mimicking the crp results.

We agree with this idea in principle but note that the output from our reporter gene, β- galactosidase, is stable within cells and tends to accumulate. This is likely to obscure the reduction in expression as cells transition from low to high cell density. Since we have demonstrated the regulatory effects of HapR and CRP both in vivo using gene knockouts, and in vitro with purified proteins, we think that our overall model is very well supported. Further experimental additions may provide an incremental advance but will not alter our overall story. Also note the unexpected increase in intracellular cAMP due to addition of glucose, in Vibrio fischeri (PMID: 26062003).

Throughout the paper it was challenging to account for the number of genes selected, the rationale for their selection, and how they were prioritized. For example, the authors acknowledged toward the end of the Results section that in their prior work, CRP and HapR binding sites were identified (line 321-22).

This is not quite what we say, and maybe the reviewer misunderstood, which is our fault. The prior work identified CRP sites whilst the current work identified HapR sites. We have made a slight alteration to the text to avoid confusion.

It is unclear whether the loci indicated in Table 1 all from this prior study. It would be useful to denote in this table the seven genes characterized in Figure 2 and to provide the locus tag for murPQ.

Again, we are unsure if we have confused the reviewer. The results in Table 1 are all HapR sites from the current work, not a prior study. However, some of these also correspond to CRP binding regions found in prior work.

The reviewer mentions “the seven genes characterised in Figure 2” but 23 targets were characterised in Figure 2a and 9 in Figure 2b. The “VC” numbers used in Figure 2 are the same as used in Table 1 so it is easy to cross reference between the two. We have added a footnote to Table 1, also referred to in the Figure 2 legend, to allow cross referencing between gene names and locus tags (including for murQP and hapR).

Of the 32 loci shown in Table 1, five were selected for further study using EMSA (line 322), but no rationale is given for studying these five and not others in the table.

This is not quite correct, we did not select 5 from the 32 targets listed in Table 1. We selected 5 targets from Table 1 that were also targets for CRP in our prior paper. This was the rationale.

Since prior work identified a consensus CRP binding motif, the authors identify the DNA sequence to which HapR binds overlaps with a sequence also predicted to bind CRP. Genome analysis identified a total of seven sites where the CRP and HapR binding sites were offset by one nucleotide as see with murPQ. Lines 327-8 describe EMSA results with several of these DNA sequences but provides no data to support this statement. Are these loci in Table 1?

This comment is a little difficult to follow, and we may have misunderstood, but we think that the reviewer is asking where the EMSA data referred to on lines 327-328 resides. We can see that the text could be confusing in this regard. We had referred to the relevant figure (Figure S6) on line 324 but did not again include this information further down in the description of the result. We have changed the text accordingly.

Using structural models, the authors predict that HapR repression requires protein-protein interactions with CRP. Electromobility shift assays (EMSA) with purified promoter DNA, CRP and HapR (Fig 5d) and in vitro transcription using purified RNAP with these factors (Figure 5e) support this hypothesis. However, the model proports that HapR "bound tightly" and that it also had a "lower affinity" when CRP protein was used that had mutations in a putative interaction interface. These claims can be bolstered if the authors calculate the dissociation constant (Kd) value of each protein to the DNA. This provides a quantitative assessment of the binding properties of the proteins.

The reviewer is correct that we do not explicitly provide a Kd. However, in both Figures 5d and 5e, we do provide very similar quantification. In 5d, our quantification is the % of the CRP-DNA complex bound by HapR (using either wild type or E55A CRP). Since the % of DNA bound is shown, and the protein concentrations are provided in the figure legend, information regarding Kd is essentially already present. In 5e, we show the % of maximal promoter activity. This is a reasonable way of quantifying the result. Furthermore, Kd is not a metric we can measure directly in this experiment that is not a DNA binding assay.

The concentrations of each protein are not indicated in panels of the in vitro analysis, but only the geometric shapes denoting increasing protein levels.

The protein concentrations are all provided in the figure legend. It is usual to indicate relative concentrations in the body of the figure using geometric shapes.

Panel 5e appears to indicate that an intermediate level of CRP was used in the presence of HapR, which presumably coincides with levels used in lane 4, but rationale is not provided.

There was no particular rationale for this, it was simply a reasonable way to do the experiment.

How well the levels of protein used in vitro compare to levels observed in vivo is not mentioned.

The protein concentrations that we use (in the nM to low μM range) are very typical for this type of work and consistent with hundreds of prior studies of protein-DNA interactions. The general rule of thumb is that 1000 molecules of a protein per bacterial cell equates to a concentration of around 1 μM. However, molecular crowding is likely to increase the effective concentration. Additionally, in vitro, where the DNA concentration is higher.

The authors are commended for seeking to connect the in vitro and vivo results obtained under lab conditions with conditions experienced by V. cholerae in niches it may occupy, such as aquatic systems. The authors briefly review the role of MurPQ in recycling of the cell wall of V. cholerae by degrading MurNAc into GlcNAc, although no references are provided (lines 146-50). Based on this physiology and results reported, the authors propose that murPQ gene expression by these two signal transduction pathways has relevance in the environment, where Vibrios, including V. cholerae, forms biofilms on exoskeleton composed of GlcNAc.

We have added a citation to the section mentioned.

The conclusions of that work are supported by the Results presented but additional details in the text regarding the characteristics of the proteins used (Kd, concentrations) would strengthen the conclusions drawn. This work provides a roadmap for the methods and analysis required to develop the regulatory networks that converge to control gene expression in microbes. The study has the potential to inform beyond the sub-filed of Vibrios, QS and CRP regulation.

As noted above, quantification essentially equivalent to Kd is already shown (% of bound substrate is indicated in figures and all protein concentrations are given in the figure legends).

Reviewer #1 (Recommendations For The Authors):

1.  As similar experiments have been performed in other Vibrios, it would be interesting to do a more detailed analysis of the similarities and differences between the species. Perhaps a Venn diagram showing how many targets were found in all studies versus how many are species specific.

We appreciate this suggestion but would prefer not to make this change. A cross-species analysis would be very time consuming and is not trivial. The presence and absence of each target gene, for all combinations of organisms, would first need to be determined. Then, the presence and absence of binding signals for HapR, or its equivalent, would need to be determined taking this into account. For most readers, we feel that this analysis is unlikely to add much to the overall story. Given the amount of effort involved, this seems a “non-essential” change to make.

2.  Line 101-Are the FLAG tagged versions of LuxO and HapR completely functional? Can they complement a luxO or hapR deletion mutant?

The activity of FLAG tagged HapR (LuxR in other Vibrio species) has been shown previously (e.g. PMIDs 33693882 and 23839217). Similarly, N-terminal HapR tags are routinely used for affinity purification of the protein without ill effect. We have not tested LuxO-3xFLAG for “full” activity, though this fusion is clearly active for DNA binding, the only activity that we have measured here, since all know targets are pulled down.

3.  Line 106-As the authors state later that there are additional smaller peaks for HapR that could be other direct targets, I think a brief mention of the methodology used to determine the cutoff for the 5 and 32 peaks for LuxO and HapR, respectively, would be informative here.

We have added a little more text to the methods section. The added text states “Note that our cut- off was selected to identify only completely unambiguous binding peaks. Hence, weak or less reproducible binding signals, even if representing known targets, were excluded (see Discussion for further details)”.

4.  Line 118-Need a reference here to the prior HapR binding site.

This has been added.

5.  Figs. 1e-What do the numbers on the x-axis refer to? Why not just present these data as bases? The authors also refer to distance to the nearest start codon, but this is irrelevant for 4/5 of the luxO targets as they are sRNAs. They should really refer to the distance to the transcription start site. Likewise, for HapR, distance to the nearest start codon is not as informative as distance to the nearest transcription start site. A recent paper used transcriptomics to map all the transcription start sites of V. cholerae, and these results should be integrated into the author's study rather than just using the nearest start codon (PMID: 25646441).

The numbers are kilo base pairs, this has been added to the axis label. We have also changed “start codon” to “gene start” (since “gene start” is also suitable for genes that encode untranslated RNAs).

Re comparing binding peak positions to transcription start sites (TSSs) rather than gene starts, this analysis would be useful if TSSs could be detected for all genes. However, some genes are not expressed under the conditions tested by PMID: 25646441, so no TSS is found. Consequently, for HapR or LuxO bound at such locations, we would not be able to calculate a meaningful position relative to the TSS. We stress that the point of the analysis is to determine how peaks are positioned with respect to genes (i.e. that sites cluster near gene 5’ ends). Also note that nearest TSSs are now shown in the revised Table 1. In some cases, these are unlikely to be the TSS actually subject to regulation (e.g. because the regulated gene is switched off).

6.  Fig. 1e-Is there directionality to the site? In other words, if a HapR binding site is located between two genes that are transcribed in opposite directions, is there a way to predict which gene is regulated? It looks like this might be the case with the list presented in Table 1, but how such determination is made and what the various symbol in Table 1 mean are not clear to me. This also has ramifications for Fig. 2a as the direction to construct the fusion is critical for the experiment.

The site is a palindrome so lacks directionality. The best prediction re regulation is likely to be positioning with respect to the nearest TSS (which is now included in Table 1). However, this would remain just a prediction and, where TSSs are in odd locations with respect to binding sites (taking into account the caveats above) predictions would be unreliable.

We are unsure which symbol the reviewer refers to in Table 1, a full explanation of any symbols used is provided in the table footnotes.

With respect to Figure 2a, if sites were between divergent genes, and met our other criteria, we tested for regulation in both directions. For example, see the divergent genes VCA0662 (classified inactive) and VCA0663 (classified repressed).

7.  Fig. 2a-It is a little disappointing that the authors use LacZ fusions to measure transcription as this is not the most sensitive reporter gene. Luciferase gene fusions would have been much more sensitive. Also, did the authors examine multiple time points. The methods only describe "mid-log phase" but some of the inactive promoters could be expressed at other time points. Also, it would be simple to repeat this experiment in different media, such as minimal with glucose or another non- CRP carbon source, to expand which promoters are expressed.

The reviewer is correct regarding the sensitivity of β-galactosidase, which is very stable and so accumulates as cells grow. Even so, this reporter has been used very successfully, across thousands of studies, for decades. We did not examine multiple timepoints. We appreciate that the 23 promoter::lacZ fusions could be re-examined using varying growth conditions but this is unlikely to impact the overall conclusions, though it could generate some new leads for future work.

8.  Fig. 2a legend-typos

This has been corrected.

9.  Line 138-I think you mean Fig. 2a here.

This has been corrected.

10.  Fig. 2b and many additional figures quantify band intensity but do not show any replication or error. Therefore, it is impossible to gauge reproducibility of these experiments.

We have added a reproducibility statement (all experiments were done multiple times with similar results) as is standard throughout the literature. Also note that there is a lot of internal replication between figures. Figure 4d and Figure 5e lanes 1-9 show essentially the same experiment (albeit with slightly different protein concentrations) and very similar results. To the same effect, Figure 5e lanes 10-18 and lanes 19-27 show the same experiment for two different mutations of the same CRP residue. Again, the results are very similar. Also see the response to your comment 15 below.

11.  Fig. 4a-lanes 2-4-the footprint does not change with additional CRP. In other words, it looks the same at the lowest concentration of CRP versus the highest concentration of CRP. The footprints for HapR look similar. This is somewhat troubling as in these types of experiments one would like to observe a dose dependent change in the footprint correlating with more DNA occupancy.

For CRP we agree but are not concerned at all by this. The site is simply full occupied at the lowest protein concentration tested. Given that the footprint exactly coincides with a near consensus CRP site (which, when mutated, abolishes CRP binding in EMSAs, and regulation by CRP in vivo) all our results are perfectly consistent. Note that i) our only aim in this experiment was to determine the positions of CRP and HapR binding ii) our conclusions are independently backed up using gel shifts and by making promoter mutations. With respect to HapR, there are changes at the periphery of the main footprint.

12.  Fig. 4e-Why does the transcriptional activation of murQP decrease with increasing concentrations of CRP? This is also seen in Fig. 5e.

In our experience, this often does happen when doing in vitro transcription assays (with CRP and many other activators). The anecdotal explanation is that, at higher concentrations, the regulator can start to bind the DNA non-specifically and so interfere with transcription.

13. The authors demonstrate in vitro that HapR requires binding of CRP to bind the murQP promoter. It would strengthen their model if they demonstrated this in vivo. To do this, the authors only need to repeat their ChIP-Seq experiment in a delta CRP mutant and the HapR signal at murQP would be lost. In fact, such an experiment would experimentally confirm which of the in vivo HapR binding sites are CRP dependent.

We agree, appreciate the comment, and do plan to do such experiments in the future as a wider assessment of interactions between transcription factors. However, doing this does have substantial time and resource implications that we cannot devote to the project at present. We feel that our overall conclusions, regarding co-operative interactions between HapR and CRP at PmurQP, are well supported by the data already provided. This also seems the overall opinion of the reviewers.

14.  Fig. 5b-I am confused by the Venn diagram. The text states that "In all cases, the CRP and HapR targets were offset by 1 bp", but the diagram only shows 7 overlapping sites. The authors need to better describe these data.

We mean that, in all cases where sites overlap, sites are offset by 1 bp (i.e. we didn’t find any sites

overlapping but offset by 2, 3 4 bp etc).

15. Line 287-288 and Fig. 5d-The authors state that HapR binds with less affinity to the CRP E55A mutant protein bound to DNA. There does seem to be a difference in the amount of shifted bands at the equivalent concentrations of HapR, but the difference is subtle. In order to make such a conclusion, the authors should show replication of the data and calculate the variability in the results. The authors should also use these data to determine the actual binding affinities of HapR to WT and the E55A mutant CRP, along with error or confidence intervals.

All of these experiments have been run multiple times and we are absolutely confident of the result. With respect to Figure 5d, this was done many times. We note that not all experiments were exact repeats. E.g. some of the first attempts had fewer HapR concentrations. Even so, the defect in HapR binding to the CRP E55A complex was always evident. The two gels to the left show the final two iterations of this experiment (these are exact repeats). The top image is that shown in Figure 5d. The lower image is an equivalent experiment run a day or so previously. Both clearly show a defect in HapR binding to the CRP E55A complex. We appreciate that our conclusion re these experiments is somewhat qualitative (i.e. that HapR binds the CRP E55A complex less readily) but this is not out of kilter with the vast majority of similar literature and our results are clearly reproducible.

16.  Fig. 6a-It is odd that the locked low cell density mutants have such a growth defect in MurNAc, minimal glucose, and LB. To my knowledge, such a growth defect is not common with these strains. Perhaps this has to do with the specific growth conditions used here, but I can't find that information in the manuscript (it should be there). Furthermore, the growth rate of the luxO and hapR mutants appears to be similar up to the branch point (i.e. slope of the curve), but the lag phage of the luxO mutant is much longer. The authors need to address these issues in relationship to previous published literature and specify their growth conditions because the results are not consistent with their simple model described in Fig 6b.

This comment is a little difficult to pick apart as it covers several different issues. We’ll try and

answer these individually.

a)     The unusual “biphasic growth curve with hapR and hapRluxO cells: We do not know why cells lacking hapR have a growth curve that appears biphasic. We can only assume that this is due to some regulatory effect of HapR, distinct from the murQP locus. Despite the unusual shape of the growth curve, the data are consistent with our conclusions.

b)     The extended lag phase of the luxO mutant in minimal media + MurNAc: We appreciate this comment and had considered possible explanations prior to submission. In the end, we left out this speculation but are happy to include it as part of our response. The extended lag phase might be expected if CRP/HapR regulation is largely critical for controlling the basal transcription of murQP. The locus is likely also regulated by the upstream repressor MurR (VC0204) as in E. coli. So, if deprepression of MurR overwhelms the effect of HapR on murQP, we think you would expect that once the cells start growing on MurNAc, the growth rates are unchanged. But the extended lag is due to the fact that it took longer for those cells to achieve the critical threshold of intracellular MurNAc-6-P necessary to drive murR derepression. Obviously, we can not provide a definitive answer.

c)     We have added further details regarding growth conditions to the methods section and the Figure 6a legend.

17.  Fig. S6-The data to this point with murPQ suggested a model in which CRP binding then enabled HapR binding. But these EMSA suggest that both situations occur as in some cases, such as VCA0691, HapR binding promotes CRP binding. How does such a result fit with the structural model presented in Fig. 5?

This is to be expected and is fully consistent with the model. Cooperativity is a two-way street, and each protein will stabilise binding of the other. Clearly, it will not always be the case that the shared DNA site will have a higher affinity for CRP than HapR (as at PmurQP). Depending on the shared site sequence, expected that sometimes HapR will bind “first” and then stabilise binding of CRP.

18. Line 354-356-The HCD state of V. cholerae occurs in mid-exponential phase and several cell divisions occur before stationary phase and the cessation of growth, at least in normal laboratory conditions. Therefore, there is not support for the argument that QS is a mechanism to redirect cell wall components at HCD because cell wall synthesis is no longer needed.

We did not intent to suggest cell wall synthesis is not needed at all, rather that there is a reduced need. We made a slight change to the discussion to reflect this.

19. Line 357-360-Again, as stated in point 16, the statement that cells locked in the HCD are "defective for growth" is an oversimplification. The luxO mutants have a longer lag phage, but they actually outgrow the hapR mutants at higher cell densities and reach the maximum yield much faster.

In fairness, we do go on to specify that the defect is an extended lag phase. Also see our response above.

Reviewer #2 (Recommendations For The Authors):

Comments to improve the text

1)  Line 103-106, line 130, line 136, etc. Details of the methods and the text directing to presentations of figures should be in the methods and/or figure legends with (Figure x) in citation after the statement. The sentences in lines indicated can be deleted from the results. Although several lines are noted specifically here, this comment should be applied throughout the entire results section.

We appreciate this comment but would prefer not to make this change (it seems mainly an issue of personal stylistic choice). It is sometimes helpful for the reader to include such information as it avoids them having to cross reference between different parts of the manuscript.

2)  Line 115. Recommend a paragraph between content on LuxO and HapR (before "Of the 32 peaks for HapR binding")

We agree and have made this change.

3)  Line 138 and Figure 1a. I am not convinced this gel shows that VC1375 is activated by HapR. Is the arrow pointing to the wrong band? There does seem to be an induced band lower down.

We understand this comment as it is a little difficult to see the induced band. This is because this is a compressed area of the gel and the transcript is near to an additional band.

4)  Line 147. Add the VC0206-VC0207 next to murQP (and the gene name murQP into Table 1).

We have added the gene name to the figure foot note. The text has been changed as requested.

5) Methods. It is essential for this paper to have detailed methods on the bacterial growth conditions. Referring to prior paper, bacteria were grown in LB (add composition...is this high salt LB often used for vibrios or low salt LB often used for E. coli). Growth is to "mid log". Please provide the OD at collection. Is mid log really considered "high density". Provide a reference regarding HapR activity at mid log to support the method. Could the earlier collection of bacteria account for missing known HapR regulated genes? In preparing the requested ç, include growth conditions for other experiments in the legends.

Note that we have included a new supplementary table, rather than a Venn diagram. We have also added further details of growth conditions as mentioned above. Also not that, for the ChIP-seq, HapR and LuxO were expressed ectopically and so uncoupled from the switch between low and high cell density.

6)  Content of Table 1, HapR Chip-seq peaks, needs to be closely double checked to the collected data as there seems to be some errors. Specifically, VC0880 and VC0882 listed under Chromosome I are most likely VCA0880 (MakD) and VCA0882 (MakB), both known HapR induced genes on Chromosome II with VCA0880 previously validated by EMSA. This notable error suggests the table may have other errors and thus requires a very detailed check to assure its accuracy.

We appreciate the attention to detail! We have double checked, thankfully this is not an error, the table is correct (even so, we have also checked all other entries in the table). As an aside, VCA0880 is one of the locations for which we see a weak HapR binding signal below our cut-off (included in the new Table S1). In cross checking between Table 1 and all other data in the paper we noticed that we had erroneously included assay data for VC0620 in Figure 2A. This was not one of our ChIP-seq targets but had been assayed at the same time several years ago. This datapoint, which wasn’t related to any other part of the manuscript, has been removed.

If VCA0880 and VCA0882 are correctly placed on Chr. I, then add comment to text that the Mak toxin genomic island found on Chromosome II in N16961 is on Chr. I in E7946. (See recent references PMID: 30271941, 35435721, 36194176, 34799450).

See above, this is not an error.

7)  Alternatively for both comments 8 & 9, are these problems of present/missing genes or misannotations the result of the annotation of E7946 gene names not aligning with gene names of N16961? (if so, in Table 1, please give the gene name as in E7946 but include a separate column with the N16961 name for cross study comparison)

See above and below, this is not an issue.

8)  Line 126-127. Also regarding Table 1, please add a column with function gene annotation. For example, VC0916 needs to be identified as vpsU. If function is unknown, type unknown in the column. This will help validate the approach of selecting "HapR target promoters where adjacent coding sequence could be used to predict protein function."

We added an extra column to Table 1 in response to a separate reviewer request (TSS locations). This leaves no space for any additional columns. Instead, to accommodate the reviewer’s request, we have added alternative gene names to the footnote.

Not following up on VCA0880 (promoter for the mak operon) is a sad missed opportunity here as it is one of the most strongly upregulated genes by HapR (PMC2677876)

As noted above, this was not an error and VCA0880 was not one of our 32 HapR targets. As such, we would not have followed this up.

9)  Figure Legends. Add a unit to the bar graphs in Figure 1e (should be kb??) This has been corrected.

10) The yellow color text labels in figures 3c, 4a, 4c are difficult to read. Can you use an alternative darker color for CRP.

We have made this slightly darker (although to our eye it is easily reliable). We haven’t changed the colour too much, for consistency with colour coding elsewhere.

11) Figure S3. Binding is misspelled. Add units to the x-axis

This has been corrected.

12) Figure S7. The text in this figure is too small to read. Figure could be enlarged to full page or text enlarged. Are these 4 the only other known regulated promoters? Could all the known alternative promoters linked to HapR be similarly probed?

We have increased the font size and included a new Table S1 for all previously proposed HapR sites.

13) Figure S8. Original images..are any of these the replicate gels (see public comment 6)

We have added a statement regarding reproducibility, and also note the internal reproducibility between different figures in our reviewer response. The gels in Figure S8 are full uncropped versions of those shown in the main figures.

Reviewer #3 (Recommendations For The Authors):

None

Whilst there were no specific recommendations from this reviewer, we have still responded to the public review and made changes if required.

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

Learn more at Review Commons

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Reply to the reviewers

Dear Editor and reviewers,

Thank you very much for the thorough assessment of our manuscript. We have carefully considered the comments and reflected most of them in the new version. We recognized the need to shorten and clarify the manuscript. Therefore, we have omitted particularly the less important passages concerning metabolism and the loss of genes encoding mitochondrial proteins, which cut the text by six pages in the current layout. We have also removed the text relating this model to eukaryogenesis. Finally, we have slightly changed the structure and linked the different sections to improve the flow of the story and to emphasize the key messages, which are the absence of mitochondria in a large proportion of oxymonads and the impact of this loss, loss of Golgi stacking and transformation to endobiotic lifestyle on selected gene inventories. We hope the manuscript is now clear and more concise and will be of interest to a broad readership interested in the evolution of eukaryotes, mitochondria and protists.

1. Point-by-point description of the revisions

Reviewer #1 (Evidence, reproducibility and clarity):

This is a very interesting paper that investigates through detailed comparative genomics the tempo and mode of the evolution of microbial eukaryotes/protists members of the Metamonada with a focus on Preaxostyla, currently the only known lineage among eukaryotes to have species that have lost, by all accounts, the mitochondria organelle all together. Notably, it includes a free-living representative of the lineage allowing potential interesting comparison between lifestyles among the Preaxostyla. This is a generally nicely crafted manuscript that presents well supported conclusions based on good quality genome sequence assemblies and careful annotations. The manuscript presents in particular (i) additional evidence for the common role of LGT from various bacterial sources into eukaryotic lineages and (ii) more details on the transition from a free-living lifestyle to an endobiotic one and (iii) the related evolution of MROs and associated metabolism.

Thank you very much for the positive assessment.

I have some comments to improve a few details:

In the introduction, lines 42-43, the last sentence should be more conservative by replacing "whole Oxymonadida" with "...all known/investigated Oxymonadida".

The sentence has been changed to: "Our results provide insights into the metabolic and endomembrane evolution, but most strikingly the data confirm the complete loss of mitochondria and every protein that has ever participated in the mitochondrion function for all three oxymonad species (M. exilis, B. nauphoetae, and Streblomastix strix) extending the amitochondriate status to all investigated Oxymonadida."

Similarly on line 62, the sentence could state "... contain 140 described...".

The sentence has been changed to: "Oxymonadida contain approximately 140 described species of morphologically divergent and diverse flagellates exclusively inhabiting digestive tracts of metazoans, of which none has been shown to possess a mitochondrion by cytological investigations (Hampl 2017)."

When discussing the estimated completeness of the genome are discussed (lines 117-120) and contrasted with the values for Trypanosoma brucei and other genomes, the author should explicitly state that these genomes are considered complete, which seems is what they imply, is that the case? If so, please provide more details to support this idea.

We have elaborated on this part also in reaction to comments of other reviewers. The text now reads: "It should be noted that, despite their wide usage, BUSCO values are not expected to reach 100% in lineages distant from model eukaryotes simply due to the true absence (or high sequence divergence) of some of the assessed marker genes. For example, various Euglenozoa representatives with highly complete genome sequences, including Trypanosoma brucei, have BUSCO completeness estimates in the range of 71-88% (Butenko et al. 2020), and representatives of Metamonada fall within the range of 60-91% (Salas-Leiva et al. 2021). Specifically in the case of oxymonad M. exilis, the improvement of the genome assembly using long-read resequencing from 2092 scaffolds to 101 contigs led to only a marginal increase of BUSCO value from 75.3 to 77.5 (Treitli et al. 2021). "

Also please see the detailed table prepared in response to reviewers 2 and 3 summarizing the presence/absence of genes from BUSCO set in the selected representatives of Metamonada and Trypanosoma brucei. The table is commented in the answer to Reviewer 3 comment (page 18)

The supplementary file named "132671_0_supp_2540708_rmsn23" is listed as a Table SX? (note: I found it rather difficult to establish exactly what file corresponds to what document referred in the main text)

We apologize for this mistake. We have checked and corrected references to tables, figures and supplementary material throughout the manuscript and hope it now does not contain any errors.

Lines 243-245, where 46 LGTs are discussed, it is relevant that the authors investigate their functional annotations. Indeed, it is suggested that these could have adaptive values, hence investigating their functional annotation will allow the authors to comment on this possibility in more details and precision. When discussing LGTs it would also be very useful to cite relevant reviews on the topic - covering their origins, functional relevance when known, distribution among eukaryotes. This is done when discussing the evolution and characteristics of MROs but not when discussing LGTs, with several reviews cited and integrated in the discussion of the data and their interpretation.

Available annotations of all putative LGT genes are provided in Supplementary_file_3 and also in the Supplementary_file_6 if the gene belongs to a manually annotated cellular system. Although we agree with the reviewer that the discussion of 46 species-specific LGTs might be interesting, for the sake of conciseness and brevity of the manuscript, we have decided not to expand the discussion further. However, note that we discuss selected cases of P. pyriformis-specific LGTs in the part “P. pyriformis possesses unexpected metabolic capacities” which follows right after the lines reviewer is referring to.

The sentence, lines 263-265, where the distribution of some LGTs are discussed, needs to be made more precise. When using the work "close" the authors presumably refer to shared/similar habitat,s or else? Entamoeba is not a close relative to the other listed taxa.

The “close relatives” mentioned in the text were meant as close relatives of all p-cresol-synthesizing taxa discussed in the paragraph, including Mastigamoeba, i.e. a specific relative of Entamoeba. We have modified the text such as to make the intended meaning easier to follow.

Lines 346-348, that sentence needs to end with a citation (e.g. Carlton et al. 2007).

The citation proposed by the reviewer has been added. The sentence was changed to: " The most gene-rich group of membrane transporters identified in Preaxostyla is the ATP-binding cassette (ABC) superfamily represented by MRP and pATPase families, just like in T. vaginalis (Carlton et al. 2007). "

In the paragraph (line 580-585) discussing ATP transporters, note that Major et al. (2017) did not describes NTTs but distantly related members of MSF transporter, shared across a broader range of organisms then the NTTs. Did the authors check if the genome of interest encoded homologues of these transporters too?

The citation has been removed; we admit that it was not the most appropriate one in the given

context. Concerning the NTT-like transporters, encouraged by the reviewer we searched for them in the Preaxostyla genome and transcriptome assemblies and found no candidates. This is not explicitly stated in the revised manuscript. The paragraph now reads: “MROs export or import ATP and other metabolites typically using transporters from the mitochondrial carrier family (MCF) or sporadically by the bacterial-type (NTT-like) nucleotide transporters (Tsaousis et al. 2008). We did not identify any homolog of genes encoding proteins from these two families in any of the three oxymonads investigated. In contrast, MCF carriers, but not NTT-like nucleotide transporters, were recovered in the number of four for each P. pyriformis and T. marina (Supplementary file 6).“

Line 920-921, I don't understand how the number 30 relates to "guarantee" inferring the directionality of LGTs events. This will be very much dataset dependent, 100 sequences might still not allow to infer directionality of LGT events. The authors probably meant to "increase the possibility to infer directionality".

We agree the original wording has not been particularly fortunate, so the sentence has changed to: "Files with 30 sequences or fewer were discarded, as the chance directionality of the transfer can be determined with any confidence is low when the gene family is represented by a small number of representatives."

Reviewer #2 (Evidence, reproducibility and clarity):

Using draft genome sequencing of the free-living Paratrimastix pyriformis and the sister lineage oxymonad Blattamonas nauphoetae, Novack et al. infer the metabolic potential of the two protists using comparative genomics. The authors conclude that the common oxymonad ancestor lost the mitochondrion/mitosome and discuss general strategies for adapting to commensal/symbiotic life-style employed by this taxon. Some elaborations on pathways go on for several paragraphs and feel unnecessarily stretched, which made those sections of the paper rather difficult to digest.

Having seen reflections on the manuscript by three reviewers we carefully reconsidered its content and attempted to make it shorter and more compact by removing some of the less substantial material. Namely, we have dispensed completely with the original last section of Results and Discussion (“No evidence for subcellular retargeting of ancestral mitochondrial proteins in oxymonads”) and made various cuts throughout other sections. We hope that the revised version makes a substantially better job of delivering the key messages of our study to the readers compared to the original submission.

This might be also be because the work, and all conclusions drawn, depend entirely on incomplete (ca. 70-80%) genome data and simple similarity searches, and e.g. no kind of biochemistry or imaging is presented to underpin the manuscripts discussion.

This is a very crude and superficial assessment of our data. We have actually good reasons to believe that the genome assemblies are close to complete. Please see the discussion on this topic below and an answer to a particular comment from reviewer 3 (page 18).

This is noteworthy in light of other protist genome reports published in the last few years that differ in this respect, including previous work by this group. And for sequencing-only data, this paper - https://doi.org/10.1016/j.dib.2023.108990 - might offer an example of where we are at in 2023.

Frankly, we do not think it is fair or relevant to compare our study to the paper pointed to by the reviewer, as that paper reports on a metagenomic study that delivers a set of metagenomically assembled genomes (MAGs) of varying quality retrieved from environmental DNA samples without providing any in-depth analysis of the gene content. Our study is very different in its scope and aims, and we are not certain what lesson we should take from this reviewer’s point. We have good reasons to believe that the datasets are close to complete. Please see the discussion on this topic below and answer to comment of reviewer 3 (page 18).

With respect to previous work of the group (Karnkowska et al. 2016 and 2019), this submission is very similar (analysis pattern, even some figures and more or less the conclusion), i.e. to say, the overall progress for the broader audience is rather incremental. Then there are also some incidents, where the data presented conflicts with the author‘s own interpretation.

It was our intention to use the previous analytical experiences and approaches, which at the same time makes the new results comparable with those published before. Although the format is intentionally similar, this work is a substantial step forward because only with our present study the amitochondrial status of the large part of Oxymonadida group can be considered solidly established. This in turn allows us to estimate the timing of the loss of mitochondrion (more than 100 MYA) demonstrating that the absence of mitochondrion in this group is not an episodic transient state but a long-established status. We do not understand what exactly the reviewer had in mind when pointing to “incidents, where the data presented conflicts with the author‘s own interpretation” – we are not aware of such cases.

The text (including spelling and grammar) needs some attention and the choice of words is sometimes awkward. The overuse of quotation marks ("classical", "simple", "fused", "hits", "candidate") is confusing (e.g. was the BLAST result a hit or a "hit").

The whole text has been carefully checked and the language corrected whenever necessary by a one of the co-authors, who is a native English speaker. The use of quotation marks has been restricted as per the reviewer’s recommendation.

In its current formn the manuscript is, unfortunately, very difficult to review. This reviewer had to make considerable efforts to go through this very large manuscript, mainly because of issues affecting to the presentation and the lack of clarity and conciseness of the text. It would be greatly appreciated if the authors would make more efforts upfront, before submission, to make their work more easily accessible both to readers and facilitate the task of the reviewers.

We admit that the story we are trying to tell is a complex one, consisting of multiple pieces whose integration into a coherent whole is a challenging task. As stated above, the reports provided by the reviewers provided us with an important stimulus, leading us to substantially modify the manuscript to make it more concise, less ambiguous when it comes to particular claims, and easier to read. We hope this intention has been fulfilled to a larger degree.

About a fifth of the two genome is missing according the authors prediction (table 1). Early on they explain the (estimated) incompleteness of the genomes to be a result from core genes being highly divergent. In light of this already suspected high divergence, using (the simplest NCBI) sequence similarity approach to call out the absence of proteins (for any given lineage) may need lineage-specific optimization. The use of more structural motif-guided approaches such as hidden Markov models could help, but it is not clear whether it was used throughout or only for the search for (missing) mitochondrial import and maturation machinery. The authors state that the low completeness numbers are common among protists, which, if true, raises several questions: how useful are then such tools/estimates to begin with and does this then not render some core conclusions problematic? The reader is just left with this speculation in the absence of any plausible explanation except for some references on other species for which, again, no context is provided. Do they have similar issues such as GC-content, same core genes missing, phylogenetic relevance?, etc.. No info is provided, the reader is expected to simply accept this as a fact and then also accept the fact that despite this flaw, all conclusions of the paper that rests on the presence/absence of genes are fine. This is all odd and further skews the interpretations and the comparative nature of the paper.

The question of the completeness of the data sets was raised also by reviewer 3 and we would like to provide an explanation at this point. First, it should be stated that there is no ideal and objective way how to measure the completeness of the eukaryotic genomic assembly. In the manuscript, we have used the best established method, adopted by the community at large, which is based on the search for a set of „core eukaryotic genes“ using a standardized pipeline BUSCO or previously popular CEGMA. The pipeline uses its own tools to identify the homologues of genes/proteins which ensures standardization of the procedure. This answers the question of reviewer 2, why we have not used more sensitive tools for these searches. We did not use them, because we followed the procedure that is the gold standard for such assessments, for comparability with other genomes and to make this as clear to the reader as possible. Although the result of the pipeline is usually interpreted as the completeness of the assembly, this is a simplification. Strictly speaking, the result is a percentage of the genes from the set of 303 core eukaryotic genes (in our case) which were detected in the assembly by the pipeline. Even in complete assemblies, the value is usually below 100% because some of the genes are not present in the organism and some diverged beyond recognition. We do not see any other way how to deal with this drawback than to compare with related complete genome assemblies acting as standards. This we have done in Supplementary file 11, where we list the presence/absence of each gene for Preaxostyla species and three highly complete assemblies of Trypanosoma brucei, Giardia intestinalis and Trichomonas vaginalis. T. brucei and G. intestinalis are assembled into chromosomes. As you can see, in these three „standards“ 63, 148 and 77 genes from the core were not detected resulting in BUSCO completeness values of 79%, 51% and 75%, respectively. 18 of the non-detected genes function in mitochondria (shown in red), which are highly reduced in some of these species, so the absence of the respective genes is therefore expected. Simply not considering these genes would increase the “completeness measure” for oxymonads by 6%. The values for our standards are not higher than the values for Preaxostyla (69-82%). In summary, the BUSCO incompleteness measure is far from ideal, particularly in these obscure groups of eukaryotes. The values received for Preaxostyla give no reason for concern about their incompleteness. See also our answer to reviewer 3 (page 18).

At the same time, we admit that the BUSCO values do not confirm the high completeness of our assemblies. So, why do we think they are highly complete? One reason is that we do not see suspicious gaps in any of the many pathways which we annotated but the main reason is the high contiguity of the assemblies. Thanks to Nanopore long read sequencing, the assembly of P. pyriformis and B. nauphoetae compose of 633 and 879 scaffolds, suggesting that there are “only” hundreds of gaps. Although this may still sound too much, it is a relatively good achievement for genomes of this size and the experience shows that a further decrease in the number of scaffolds would allow the detection of additional genes but not in huge numbers. As we have shown for M. exilis (Treitli et al. 2021, doi:10.1099/mgen.0.000745) the decrease from 2 092 scaffolds to 101 contigs, i.e., filling almost 2 000 gaps, allowed the prediction of additional 1 829 complete gene models, of which 1 714 were already present in the previous assembly but only partially and just 115 were completely new. None of these newly predicted genes was functionally related to the mitochondrion. Thus, we infer the chance that all mitochondrion-related genes are hidden in the gaps of assemblies is very low.

We have provided these arguments in a condensed form in the text following the description of genome assemblies: “It should be noted that, despite their wide usage, BUSCO values are not expected to reach 100% in lineages distant from model eukaryotes simply due to the true absence (or high sequence divergence) of some of the assessed marker genes. For example, various Euglenozoa representatives with highly complete genome sequences, including Trypanosoma brucei, have BUSCO completeness estimates in the range of 71-88% (Butenko et al. 2020), and representatives of Metamonada fall within the range of 60-91% (Salas-Leiva et al. 2021). Specifically in the case of oxymonad M. exilis, the improvement of the genome assembly using long-read resequencing from 2092 scaffolds to 101 contigs led to only a marginal increase of BUSCO value from 75.3 to 77.5 (Treitli et al. 2021).”

As a side note, this will also influence the number of proteins absent in other lineages and as such has consequences on LGT calls versus de novo invention. For the cases with LGT as an explanation, it would help to briefly discuss the candidate donors and some details of the proteins in the eco-physiological context (e.g. lines 263-268 suggest that HPAD may have been acquired by EGT which was facilitated by a shared anaerobic habitat and also comment on adaptive values for acquiring this gene). Exchanging metabolic genes via LGT (Line 163) blurs the differences between roles and extent of LGT in prokaryote vs eukaryote, and therefore is exciting and could use support/arguments other than phylogenies. I guess the number of reported LGTs among protists (whatever the source) over the last decade has by now deflated the novelty of the issue in more general; a report of the numbers is expected but they alone won't get you far anymore in the absence of a good story (such as e.g. work on plant cell wall degrading enzymes in beetles).

We agree with the reviewer that the cases of LGT involving Preaxostyla would deserve more discussion in the manuscript. On the other hand, we also agree that none of them provides such a “cool” story that would deserve a special chapter or even a separate paper. Therefore, we have decided, also with regard to keeping the text in a reasonable dimension, not to expand the discussion of LGTs with the exception of HgcAB, where some new information has been included and the phylogeny of the genes updated. Please note that we had discussed in the original manuscript the donor lineages and ecological/biochemical context in the cases of GCS-L2, HPAD, UbiE, and NAD+ synthesis and this material has been kept also in the revised version.

It would help to clarify which parts of the mitochondrial ancestor were reduced during the process of reductive evolution at what time in their hypothesized trajectory. For instance, loosing enzymes of anaerobic metabolism conflicts with the argued case of an aerobic (as opposed to facultative anaerobic) mitochondrial ancestor followed by gains of anaerobic metabolism in the rest of the eukaryotes via LGT, and some papers the authors themselves cite (e.g. the series by Stairs et al.). There is no coherent picture on LGT and anaerobic metabolism, although a reader is right to expect one.

These are very interesting questions, that would fill a separate article. In the manuscript, we focus on the Preaxostyla lineage only and there the trajectory seems relatively simple: replacement of the mitochondrial ISC by cytosolic SUF in the common ancestor of Preaxostyla, loss of methionine cycle and in in consequence mitochondrial GCS and the mitochondrion itself. We have modified the first conclusion paragraph in this sense and it now reads the following:

“The switch to the SUF pathway in these species has apparently not affected the number of Fe-S-containing proteins but led to a decrease in the usage of 2Fe-2S clusters. The loss of MRO impacted particularly the pathways of amino acid metabolism and might relate also to the loss of large hydrogenases in oxymonads. “

It is not clear to us how to understand the reviewer’s remark concerning the conflict between loss of enzymes of anaerobic metabolism and the (presumed) aerobic nature of the mitochondrial ancestor. Provided that we read the reviewer’s rationale correctly, is it really so implausible that the anaerobic metabolism gained laterally by a particular lineage was then secondarily lost in specific descendant lineages? As a clear example demonstrating the feasibility of such an evolutionary pattern consider the evolution of plastids. There is no doubt these organelles move across eukaryotes by secondary or higher-order endosymbiosis or kletoplastidy, establishing themselves in lineages where there was no plastid before. Secondary simplification of such plastids, e.g. by the loss of photosynthesis, in its extreme form culminating in the complete loss of the organelle, has been robustly documented from several lineages, such as Myzozoa (e.g., https://pubmed.ncbi.nlm.nih.gov/36610734/). Hence, we see absolutely no reason to rule out the possibility that the ancestral mitochondrion was obligately aerobic and enzymes of anaerobic metabolism spread secondarily by eukaryote-to-eukaryote LGT, with their secondary loss in particular lineages. We really do not see any conflict here and we do not agree with the interpretation provided by the reviewer. That said, we admit that the discussion on the earliest stages of mitochondrial evolution is not an essential ingredient of the story we try to tell in our manuscript, so to avoid any unnecessary misunderstanding we have removed the original last sentence of Conclusions (“Thorough searches revealed …”) from the revised manuscript.

In light of their data the authors also discuss the importance of the mitochondrion with respect to the origin of eukaryotes:

First, the mitochondrion brought thousands of genes into the marriage with an archaeon, surely hundreds of which provided the material to invent novel gene families through fusions and exon shuffling and some of which likely went back and forth over the >billion years of evolution with respect to localizations. The authors look at a minor subset of proteins (pretty much only those of protein import, Fig. 6) to conclude, in the abstract no less: „most strikingly the data confirm the complete loss of mitochondria and every protein that has ever participated in the mitochondrion function for all three oxymonad species." I do not question the lack of a mitochondrion here, but this abstract sentence is theatrical in nature, nothing that data on an extant species could ever proof in the absence of a time machine, and is evolutionary pretty much impossible. A puzzling sentence to read in an abstract and endosymbiont-associated evolution.

We feel that the reviewer is putting too much emphasis on an aspect of our original manuscript that is rather peripheral to its major message. Indeed, the manuscript is not, and has never been thought to be, primarily about eukaryogenesis and the exact role the mitochondrion played in it. We are, therefore, somewhat reluctant to react in full to the very long and complex argument the reviewer has raised in his/her report, so we keep our reaction at the necessary minimum. Concerning the criticized sentence in the original version of the abstract, it alluded to a section of the manuscript (“No evidence for subcellular retargeting of ancestral mitochondrial proteins in oxymonads”) that we have removed from the revised version, and hence we have modified also the abstract accordingly by removing the sentence. We still think our original arguments were valid, but apparently, much more space and more detailed analyses are required to deliver a truly convincing case, for which there is no space in the manuscript.

Second, using oxymonads as an example that a lineage can present eukaryotic complexity in the absence of mitochondria and conflating it with eukaryogenesis is a logical fallacy. This issue already affected the 2019 study by Hampl et al.. We have known that a eukaryote can survive without an ATP-synthesizing electron transport chain ever since Giardia and other similar examples and the loss of Fe-S biosynthesis and the last bit of mitosome (secondary loss) doesn't make a difference how to think about eukaryogenesis. It confuses the need and cost to invent XYZ with the need and cost of maintenance. How can the authors write "... and undergo pronounced morphological evolution", when they evidently observe the opposite and show so in their Fig. 1? The authors only present evidence for reductive evolution of cellular complexity with the loss of a stacked Golgi. What morphological complexity did oxymonads evolve that is absent in other protists? A cytosolic metabolic pathway doesn't count in this respect, because it is neither morphological, nor was it invented but likely gained through LGT according to the authors. This is quite confusing to say the least. A recent paper (https://doi.org/10.7554/eLife.81033) that refers to Hampl et al. 2019 has picked this up already, and I quote: "Such parasites or commensals have engaged an evolutionary path characterized by energetic dependency. Their complexity might diminish over evolutionary timescale, should they not go extinct with their hosts first." Here the authors raise a red flag with respect to using only parasites and commensals that rely on other eukaryotes with canonical mitochondria as examples. If we now look at Fig. 1 of this submission, Novak et al. underpin this point perfectly, as the origin of oxymonads is apparently connected to the strict dependency on another eukaryote (or am I wrong?), and they support the prediction with respect to complexity reducing after the loss of mitochondria - mitosome gone, Golgi almost gone. What's next? This is a good time to remember that extant oxymonads are only a single picture frame in the movie that is evolution, and their evolution might be a dead-end or result in a prokaryote-like state should they survive 100.000s to millions of years to come.

It seems that in this point the reviewer is particularly concerned with the following sentence that is part of the Introduction and which relates to the existence of amitochondrial eukaryotes we are studying: “The existence of such an organism implies that mitochondria are not necessary for the thriving of complex eukaryotic organisms, which also has important bearings to our thinking about the origin of eukaryotes (Hampl et al. 2018).“ Even after re-reading the sentence we confess we stay with it and find it perfectly logical. Nevertheless, we decided to omit it from the text so as not to distract from the main topic of the study.

Next, when mentioning “… pronounced morphological evolution” we mean the evolution of four oxymonad families (Streblomastigidae, Oxymonadidae, Pyrsonymphidae and Saccinobaculidae) comprising almost a hundred described species with often giant and morphologically elaborated cells that evolved from a simple Trimastix-like ancestor (Hampl 2017, Handbook of Protists, 0.1007/978-3-319-32669-6_8-1). This is a fact that can hardly be dismissed. Also, given the current oxymonad phylogenies (Treitli et al. 2018, doi.org/10.1016/j.protis.2018.06.005) and the reported absence of a mitochondrion in M. exilis, B. nauphoetae, and S. strix we can infer that the mitochondrion was lost in the common ancestor of the three species at latest. This organism must have lived more than 100 MYA, as at that time oxymonads were clearly diversified into the families (Poinar 2009, 10.1186/1756-3305-2-12). So, these organisms indeed have lived without mitochondria for at least 100 MY. We think that these facts and our inferences based on them are solid enough to keep in the conclusion the following statement: “This fact moves this unique loss to at least 100 MYA deep past, when oxymonads had been already diversified (Poinar 2009), and shows that a eukaryotic lineage without mitochondria can thrive for eons and undergo pronounced morphological evolution, as is apparent from the range of shapes and specialized cellular structures exhibited by extant oxymonads (Hampl 2017).” Furthermore, as documented in Karnkowska et al. 2019 (https://pubmed.ncbi.nlm.nih.gov/31387118/), apart the loss of the mitochondrion oxymonads are surprisingly “normal” and complex eukaryotes, in fact much less reduced than, e.g., Giardia, Microsporidia, or even S. cerevisiae (in terms of the number of genes, introns, etc.). We strongly disagree with the claim that “Golgi is almost gone” in oxymonads, and our manuscript shows exactly the opposite. Viewing oxymonads as a lineage heading towards a prokaryote-like simplicity is dogmatic and ignores the known biology of these organisms.

Some more thoughts: Line 47-52: Hydrogenosome or mitosome is a biological and established label as (m)any other and I find the use of the word "artificial" in this context strange. While the authors are correct to note that there is a (evolutionary) continuum in the reduction - obviously it is step by step - they exaggerate by referring to the existing labels as "artificial". You make Fe-S clusters but produce no ATP? Well, then you're a mitosome. It's a nomenclature that was defined decades ago and has proven correct and works. If the authors think they have a better scheme and definition, then please present one. Using the authors logic, terms such as amyloplast or the TxSS nomenclature for bacterial secretions systems are just as artificial. As is, this comes across as grumble for no good reason.

We agree that the original wording sounded like unwarranted grumbling and we have changed the sentence in the following way: "However, exploration of a broader diversity of MRO-containing lineages makes it clear that MROs of various organisms form a functional continuum (Stairs et al. 2015; Klinger et al. 2016; Leger et al. 2017; Brännström et al. 2022)."

Line 158: A duplication-divergence may also explain this since sequence similarity-based searches will miss the ancestral homologues.

We do not disagree about this, in fact, the gene the reviewer’s point is concerned with for sure is a result of duplication and divergence, as it belongs to a broader gene family (major facilitator superfamily, as stated in the manuscript) together with other distant homologs. Nevertheless, this is not in conflict with our conclusion that it “may represent an innovation arising in the common ancestor of Metamonada”.

Lines 201-202: Presence of GCS-L in amitochondriate should be explained in light of this group once having a mitochondrion, which then makes ancestral derivation and differential loss (as invoked for Rsg1) also a likely explanation along with eukaryote-to-eukaryote LGT.

Yes, this most likely holds for the standard paralogue GCS-L1 (in P. pyriformis PAPYR_5544), which has the expected distribution and phylogenetic relationships and is absent in oxymonads. The discussion is, however, mainly about the rare, divergent and until now overlooked paralogue GCS-L2 (in P. pyriformis PAPYR_1328), which we found only in three distantly related eukaryote groups, Preaxostyla, Breviatea, and Archamoebae, which strongly suggests inter-eukaryotic LGT.

Lines 356-392: Describes plenty of genomic signal for Golgi bodies but simultaneously cites literature suggesting the absence of a morphologically an identifiable Golgi in oxymonads. An explicit prediction regarding what to observe in TEM for the mentioned species might be nice to stimulate further work.

We thank the reviewer for their suggestion and are glad that they are enthusiastic about this aspect of the manuscript. Unfortunately, the morphology of unstacked Golgi ranges from single cisternae (yeast, Entamoeba), vesicles (Mastigamoeba), and a “tubular membranous structure” in Naegleria. Therefore, no strong prediction is possible of what the oxymonad Golgi might look like under light or TEM. However, the data that we have provided should lead to molecular cell biological analyses aimed at identifying the organelle, giving target proteins to tag or against which to create antibodies as Golgi markers. An additional sentence to this effect has been added to the manuscript, “They also set the stage for molecular cell biological investigations of Golgi morphological variation, once robust tools for tagging in this lineage are developed.”

Lines 414: The preceding paragraphs in this result section describes only the distribution, without mentioning origins - a sweeping one-line summary that proclaims different origin needs some context and support. Furthermore, the distribution of glycolytic enzymes might indeed be patchy, but to suggest it represents an 'evolutionary mosaic composed of enzymes of different origins' without discussing the alternative of a singular origin and different evolutionary paths (including a stringer divergence in one vs. another species) discredits existing literature and the authors own claim with respect to why BUSCO might fail in protists.

The part of the text about glycolysis the reviewer alluded to has been removed while shortening the manuscript.

Line 486: How uncommon are ADI and OTC in lineages sister to metamonada?

This is an interesting but difficult question. Firstly, we are uncertain what is the sister lineage to Metamonada. Discoba, maybe, but a recent unpublished rooting of the eukaryotic tree does not support it (https://pubmed.ncbi.nlm.nih.gov/37115919/). Generally, the individual genes of the pathway (ADI, OTC and CK) are quite common in eukaryotes, but the combination of all three is rare (Metamonada, the heterolobosean Harpagon, the green algae Coccomyxa and Chlorella, the amoebozoan Mastigamoeba, and the breviate Pygsuia), see figure 1 in Novak et al 2016, doi: 10.1186/s12862-016-0771-4.

Line 504: It might help an outside reader to include a few lines on consequences and importance of having 2Fe-S vs 4Fe-S clusters and set an expectation (if any) in Oxymonads.

We apologize for omitting this explanation. The 2Fe-2S proteins are more common in mitochondria where 2Fe-2S clusters are synthesized in the early pathway of FeS cluster assembly, while the cytosolic CIA pathways produce 4Fe-4S clusters (https://pubmed.ncbi.nlm.nih.gov/33007329/). The original expectation therefore is that species without mitochondria should not have 2Fe-2S cluster proteins. Obviously, the switch to the SUF pathway affects this expectation as we do not know, what type of cluster this pathway produces in oxymonads (https://www.biorxiv.org/content/10.1101/2023.03.30.534840v1). For the sake of brevity, we have included a short statement as the beginning of the sentence in question, which now reads as follows: “As 2Fe-2S clusters are more frequent in mitochondrial proteins, the higher number of 2Fe-2S proteins in P. pyriformis compared to the oxymonads may reflect the presence of the MRO in this organism.”

Any explanations on what unique selection pressures and gene acquisition mechanisms may be operating in P. pyriformis which might allow for the unique metabolic potential?

Every species exhibits a unique combination of traits that results from changing selection pressures imposed on historical contingency (including neutral evolutionary processes such as genetic drift). We lack real understanding of these factors for a majority of taxa including the familiar ones, so we should not expect to have a good answer to the reviewer’s question. In fact, we do not know how unique is the particular combination of P. pyriformis traits discussed in our manuscript, as there has been no comprehensive comparative analysis that would include ecologically and evolutionarily comparable taxa. We note that Paratrimastix represents only a third free-living metamonad with a sequenced genome (together with Kipferlia and Carpediemonas), so more data and additional analyses are needed to be in a position when we may start hoping answers to questions like the one posed by the reviewer are in reach.

** Referees cross-commenting** To R3: Hampl et al. 2019, to which Novak et al. refer, is about eukaryogensis and that is exactly the context in which this is discussed again and what Raval et al. 2022 had decided to touch upon. If the authors do not bring this up in light of the ability to evolve (novel) eukaryote complexity, then what else? Maybe they can elaborate, especially with respect to energetics to which they explicitly refer to in 2019 (and here). And with respect to text-book eukaryotic traits (and the evolution of new morphological ones), I do not see any new ones evolving in any oxymonad, but reduction as Novak et al. themselves picture it in this submission. Is a change in the number of flagella pronounced morphological evolution? Maybe for some, but I believe this needs to be seen in light of the context of how they discuss it. I see a reduction of eukaryotic complexity and not a gain. They have an elaborate section on the loss of Golgi characteristics (and a figure), but I fail to read something along the same lines with respect to the gain of new morphological traits. Again, novel LGT-based biochemistry does not equal the invention of a new morphology such as a new compartment. Oxymonads depend on mitochondria-bearing eukaryotes for their survival or don't they? This is the main point, and if evidence show that I am wrong, then I will be the first to adapt my view to the data presented.

While we do see the logic of the reviewer’s point, a good reply would have to be too elaborate and certainly beyond the scope of the current manuscript. As the reviewers’ reports led us to reconsider the structure of the manuscript and to make it more focused and concise, we decided to simplify the matter by removing the allusions to eukaryogenesis, realizing that it is perhaps more suitable for a different type of paper (opinion, review). The comment on the evolution of complex morphology has been answered previously (see above).

I have concerns with the presentation of a narrative that in my opinion is too one-sided and that has been has been publicly questioned in the community (in press, at meetings, personally). For the benefit of science and of the young authors on this study, this reviewer feels strongly that these issues should be taken very seriously and discussed openly in a more balanced way. . We only truly move forward on such complex topics, if we allow an open and transparent discussion.

We agree that opinions on specific details of eukaryogenesis are divided in the community and that the topic requires a nuanced discussion for which there is perhaps no place in the current manuscript. As stated in the reply to the previous point, we have removed the discussion of the implications of our current study to eukaryogenesis from the revised manuscript.

Having said that, I am happy that R3 has picked up exactly the same major concerns as I did with respect to e.g. the phrasing on mito (gene) loss and the BUSCO controversy.

We appreciate these comments and hopefully have resolved the concern in the previous answers.

Reviewer #2 (Significance):

Using draft genome sequencing of the free-living Paratrimastix pyriformis and the sister lineage oxymonad Blattamonas nauphoetae, Novack et al. infer the metabolic potential of the two protists using comparative genomics. The authors conclude that the common oxymonad ancestor lost the mitochondrion/mitosome and discuss general strategies for adapting to commensal/symbiotic life-style employed by this taxon. Some elaborations on pathways go on for several paragraphs and feel unnecessarily stretched, which made those sections of the paper rather difficult to digest. This might be also be because the work, and all conclusions drawn, depend entirely on incomplete (ca. 70-80%) genome data and simple similarity searches, and e.g. no kind of biochemistry or imaging is presented to underpin the manuscripts discussion.

We have addressed the concern about the possible incompleteness of our genome data above, demonstrating it is not substantiated ad stems from an inadequate interpretation of quality measures we provide in the manuscript. We hope that the revised manuscript, which is streamlined and more concise compared to the initial submission, conveys the key messages in a substantially more persuasive way and will be appreciated by a broad community of readers.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary: The genome sequences of two members of the protist group Preaxostyla are presented in this manuscript: Paratrimastix pyriformis and Blattamonas nauphoetae. The authors use a comparative genomics and phylogenetic approaches and compare the new genome datasets with three previously available genomes and transcriptomes from the group. The availability of genome-scale data from five Preaxostyla species is powerful to address interesting basic evolutionary questions. A substantial part of the manuscript is spent on testing the hypothesis of mitochondrial loss in the oxymonad lineage, which turns out to be supported. The datasets are also explored regarding the role of lateral gene transfer in the group, metabolic diversification and the evolution of Golgi.

Major comments: I find the manuscript very interesting with many different fascinating results presented. However, the manuscript is very long. Two genome sequences are presented and it is not clear to me what the main question was when this project was initiated and why these two species was selected to answer this question. I do not see an obvious reason for sequencing the P. pyriformis genome if the mitochondrial loss was the main question (given that a transcriptome was already available). Why not spend the time and resources on a member of Preoxystyla, which lacked previous data? The authors should more clearly state why these organisms were chosen to answer the main question or questions of the study.

We are sorry for having done a poor job when explaining the choice of the taxa for the comparison. The idea was to sample an outgroup of oxymonads (P. pyriformis) and a representative of other clades of oxymonads than M. exilis (B. nauphoetae and S. strix) for which it was feasible to obtain the data, or the data were already available. Obviously, more representatives of morphologically a probably also genetically diverse oxymonads should be investigated (e.g. Pyrsonympha, Oxymonas, Saccinobacullus) and we have such a plan but these organisms are difficult to work with. We considered it necessary to sequence the genome of P. pyriformis, and not rely on the transcriptome only, to avoid the issue of data set incompleteness (raised also by R2). Transcriptomes by nature provide an incomplete coverage of the full gene complement of the species, while our genome assemblies are close to complete, as we explain elsewhere.

The evolution of MROs have received substantial attention from the protist research community since the 1990's. During this period the mitochondrial organelle have been considered essential for eukaryotes. Therefore, the result presented in the manuscript has a high significance. However, I am not convinced that it is appropriate to use the term "evolutionary transition" for the mitochondrial loss. The loss of MRO is the endpoint of a gradual change of the internal organisation of the cell that probably started when the ancestor of these organism adapted to an anaerobic lifestyle. The last step described in the manuscript probably had little impact on how these organisms interacted with their environment. The presence or absence of biosynthesis of p-cresol by some, but not all, Preaxystyla probably is much more significant from an ecological point of view. My point is that the authors need to consider how they use the term evolutionary transition and be explicit about that.

We appreciate the comment concerning the use of the term “evolutionary transition”. Nevertheless, we believe there is no real consensus in the literature on what is and what is not an “evolutionary transition”, and the application of the term to specific cases is more or less arbitrary. For a lack of a standardized or better terminology, we have kept the term to refer to three evolutionary changes in the evolution of the Preaxostyla lineage that are particularly important from the cytological or ecological perspective, i.e. dispensing with the mitochondrion, reorganizing the Golgi apparatus by losing the stacked arrangement of the cisternae, and gaining the endobiotic life style.

In the abstract the main finding is describes as "the data confirm the complete loss of mitochondria and every protein that has ever participated in the mitochondrion function for all three oxymonad species (M. exilis, B. nauphoetae, and Streblomastix strix) extending the amitochondriate status to the whole Oxymonadida.". I find this a really interesting observation, but I do find the wording a bit too bold for several reasons: • Not every protein that has participated in the mitochondrial function is known. • Mitochondrial proteins could be present in oxymonads, but divergent beyond the detection limit for existing methods. • Genes for one or several mitochondrial proteins could be present in one or more oxymonad genomes, but remain undetected due to the incomplete nature of the datasets.

Although I do think that the authors' claim very well could be true, I don't think their data fully support it. Therefore, it needs to be rephrased.

As a result of our decision to streamline the manuscript by removing the final part of Results and Discussion (“No evidence for subcellular retargeting of ancestral mitochondrial proteins in oxymonads”, the revised manuscript no longer support the statement “the data confirm the complete loss of … every protein that has ever participated in the mitochondrion function for all three oxymonad species” that is criticized by the reviewer, and hence the statement has been removed from the abstract. This addresses bullet point 1. As for bullet points 2 and 3, the proof of absence is in principle impossible to deliver, and we have been fighting with this already in the Karnkowska et al. 2016 paper. Although our certainty will never reach 100% (this is in fact impossible for a scientific, i.e., falsifiable, hypothesis), the mounting of evidence through studies gives the hypothesis on the amitochodriate status of oxymonads more and more credit. The genes for mitochondrial marker proteins have not been detected by the most sensitive methods available neither in the first genome assembly of M. exilis (Karnkowska et al. 2016), nor in the improved M. exilis genome assembly composed of only 101 contigs (Treitli et al. 2021), nor in either of the other two oxymonad species investigated here. On the other hand, they were readily detected in the data sets of P. pyriformis and T. marina. What is the probability that these genes always hide in the assembly gaps, or that they have all escaped recognition? Obviously, this probability is not zero, but we believe it is approaching so low values that it is reasonably safe to make the conclusion on the amitochondriate status of these species.

The sentence was changed to: "Our results provide insights into the metabolic and endomembrane evolution, but most strikingly the data confirm the complete loss of mitochondria for all three oxymonad species investigated (M. exilis, B. nauphoetae, and Streblomastix strix), suggesting the amitochondriate status may be common to Oxymonadida."

The third point maybe could be analysed further. BUSCO scores are reported, but also argued not being reliable for this group of organisms (which is true). Would it, for example, be useful to analyse how large fraction of the BUSCO proteins found in all non-Preoxystyla metamonada genomes that are present in the various Preoxystyla datasets?

We provide a comprehensive answer to a similar comment of reviewer 2 above (page 6-8). We performed the requested analysis and provide the result in Supplementary file 11. In this table, we record presence/absence of each gene from the BUSCO set for our data sets and the highly complete “standard” datasets of Trypanosoma brucei, Giardia intestinalis and Trichomonas vaginalis. Of the 303 genes, 117 were present in all data sets and 17 in none (see column I). 20 were present only in Trypanosoma and not in metamonads. 6 were present in all Preaxostyla and absent in other metamonads (Trichomonas and Giardia), 44 were present in all Preaxostyla and Trichomonas and absent in Giardia, suggesting high divergence of this species. Only 23 (marked by *) were present in the three “standard” genomes and absent in one or more Preaxostyla species. Of those 8 and 8 were absent specifically in S. strix and P. pyriformis, respectively, but only 1 was absent specifically in M. exilis and no such case was observed in B. nauphoetae. We conclude that this non-random pattern argues for lineage-specific divergence rather than incomplete data sets, particularly in the case of M. exilis and B. nauphoetae.

Line 160-161: 15 LGT events specific for the Preaxostyla+Fornicata clade is reported. This is an exciting finding because it supports a phylogenetic relationship between these two groups. But such an argument is only valid if the observed pattern is more common than the alternative hypotheses (Preaxostyla+Parabasalids and Fornicata+Parabasalids). How many LGT events support each of these groupings? How are these observation affected by the current taxon sampling with the highest number of datasets from Fornicata? How were putative metamonada-to-metamonada LGTs treated in this context?

19 LGT are uniquely shared between Preaxostyla+Parabasalids, which is more than the number of shared LGTs between Preaxostyla and Fornicata. No common LGT was unique to Fornicata+Parabasalids. However, the latter is a direct consequence of our investigation method, which involved reconstruction phylogenies of genes present in Preaxostyla, and not across all metamonads. So, we do not have a way to investigate LGT gene families uniquely shared between Fornicata and parabasalids.

When it comes to the effect of taxon sampling, we agree that it is possible that the number of genes of horizontal origin shared between parabasalids and Preaxostyla is underestimated because of the lower taxon sampling in parabasalids. However, it is still larger (19) than the number of LGTs shared uniquely between fornicate and Preaxostyla (15). In addition, while the taxon sampling is larger in fornicates, it also contains some representatives of closely related lineages (e.g., Chilomastix caulleryi and Chilomastix cuspidate) which, while they increase the number of fornicate representatives, does not increase the detection of shared genes between fornicates and Preaxostyla. Altogether, it's difficult to estimate how the current taxon sampling is biasing the detection of LGTs one way or another.

Regarding metamonad-to-metamonad putative LGTs: we did not consider this possibility for the sake of not overestimating the number of gene transfers for two main reasons. First of all, our LGT detection relies on the incongruence between species tree and gene tree. The closer the lineages are in the species tree, the more difficult it is to interpret any incongruence in the gene tree as single protein phylogenies are notoriously poorly resolved because they rely on the little phylogenetic signal contained in few amino-acid positions. Because of this, small incongruences with the species tree could either reflect recent LGT events between metamonads, or simply blurry phylogenetic signal. Second, we can certainly use the argument that a limited taxonomic distribution among metamonads favors an LGT event between them. However, here again, the closer the lineages involved are, the more difficult it is to distinguish a scenario where one lineage was the recipient of an LGT from prokaryote before donating it to another metamonad, from a scenario involving a single ancestral LGT from prokaryotes to metamonads, followed by differential loss, leading to a patchy taxonomic distribution. Finally, we are working with both limited taxon sampling and incomplete genomic/transcriptomic data, which makes it more difficult to identify true absences. For all these reasons, we chose to be conservative and invoke the smallest number of LGT events.

The authors have used a large-scale approach to make single-gene trees for inferences of LGT. In other parts of the manuscript inferences of evolutionary origins of single genes are made without support of phylogenetic trees. I find this inconsistent and argue that the hypothesis of the origin of a specific protein should be tested with the same rigor whether it is a putative LGT, gene duplication, gene loss or an ancestral member of LECA. Specific cases where I think a phylogenetic analysis is needed includes: • Line 222-223: It is concluded that Rsg1 is a component of LECA. • Line 307: HgcAB are argued to be acquired by LGT of a whole opeon. • Lines 350-355: It is unclear how the different numbers of transporters are interpreted (loss or expansion by duplication). This could be address with phylogenetics. • Lines 407-408: A tree should support the claim of LGT origin. (PFP) • Lines 414-415: The different origins of glycolytic enzymes should be supported by data or references. • Line 486: Trees or a reference (if available) should support the claim for LGT.

As requested, trees were constructed for HgcA, HgcB, PFP and the transporters AAAP, CTL, ENT, pATPase, and SP. Citations were added for the glycolytic enzymes and the ADI pathway. No tree for Rsg1 is needed, as this is a eukaryote-specific protein lacking any close prokaryotic relatives. The inference on its presence in the LECA is based on the phylogenetically wide, however patchy, distribution across the eukaryote phylogeny. Testing possible eukaryote-eukaryote LGTs is hampered by a limited phylogenetic signal in the short and rapidly evolving Rsg1 sequences, resulting in very poorly resolved relationships among Rgs1 sequence in a tree we attempted to make (data not shown). For this reason, we opt for not presenting any phylogenetic analysis for Rsg1.

Lines 530-531 and 773-774: "The switch to the SUF pathway in these species has apparently not affected the number of Fe-S-containing proteins but led to a decrease in the usage of 2Fe-2S clusters." I find it difficult to evaluate if the data support this because no exact numbers or identities are given for 2Fe-2S and 4Fe-4S proteins in the various genomes in Suppl. Fig. S4 or Supplementary file 4.

The functional annotation of all detected FeS clusters containing proteins is provided in Supplementary Table S8 including the types of predicted clusters (columns G or F). Basically, the only putative 2Fe2S cluster containing proteins in species of oxymonad is xanthine dehydrogenase, while Paratrimastix and Trimastix contain also 2Fe2S cluster-containing ferredoxins and hydrogenases.

The method used in the paper varies between the different parts of the paper. One example is single gene phylogenies, which are described three times in the method section [Lines 959-973, lines 1011-1034, lines 1093-1101], in addition to the automated approach within the LGT detection pipeline lines 923-926]. The approaches are slightly different with, for example, different procedures for trimming. This makes it difficult to know how the different presented analyses were done in detail. No rationale for using different approaches is given. At the least, it should be clear in the method section which approach was used for which analysis.

The reviewer is correct, and we apologize for the inconsistency. The reason is only historical –the analyses were performed by different laboratories in different periods of time. We believe this fact does not make our results less robust, although it does not “look” nice and makes the description of the methods employed longer. We have double-checked the description and introduced slight changes as to make it maximally clear which method has been used for particular analyses presented in the Results and Discussion.

Specific comments on single gene phylogenies:

• Line 966-967: Why max 10 target sequences?

The limit of 10 was applied in order to keep the datasets in manageable dimensions. The sentence has been changed to: " In order to detect potential LGT from prokaryotes while keeping the number of included sequences manageable, prokaryotic homologues were gathered by a BLASTp search with each eukaryotic sequence against the NCBI nr database with an e-value cutoff of 10-10 and max. 10 target sequences.”

• Lines 996-998: Is it a problem that these are rather old datasets?

Although the publications are slightly older the set of queries is absolutely sufficient for the purpose.

Minor comments: I appreciate that many data is included as supplementary material. However, the organisation of the data could be improved. The numbering of the files is not included in their names or within the files, as far as I could find. Descriptions of the files are often missing and information on the annotation such as colour coding is not always included. These aspects of the supplementary material needs to be strengthened in order to make it more useful. Specific comments: • Supplementary file 1, Table 1: accession numbers are missing. Kipferlia bialta appears to have a much smaller number of sequences than reported in the publication. The file consists of three tables and it would be very helpful if the reference in the main manuscript indicate the table number. • Supplementary file 4: The trees lack proper species names and a documented colour coding. There are multiple trees in the file, which make it difficult to find the correct tree. I would appreciate if the different trees were labelled A, B, C, etc., and if these were used in the main text.

Supplementary file 1: Accession numbers were added.

Supplementary file 4: Species names and alphabetical labelling were added. Colour coding was explained in the text at the first mention of the file: "(Supplementary file 4 H; Preaxostyla sequences in red)."

o There is no HPAD-AE tree (as indicated on line 258), but a HPAD tree. Which part of the tree contain the described fusion protein?

Thank you for spotting the mistake. There should have been “HPAD” instead of “HPAD-AE” indicated in the text. The sentence has been changed to:" The P. pyriformis HPAD sequence is closely related to its homolog in the free-living archamoebid M. balamuthi (Supplementary file 4 K), the only eukaryote reported so far to be able to produce p-cresol (Nývltová et al. 2017)."

o Line 280-281: "UbiE homologs occur also in some additional metamonads, including the oxymonad B. nauphoetae and certain fornicates." These sequences should be clearly highlighted in the tree.

We discovered these additional UbiE homologs only after the tree presented in the supplement had been constructed, so these sequences are missing from it. To ensure consistency we have decided to remove the remark on the presence of UbiE homologs metamonads other than P. pyriformis, so it is no longer part of the revised manuscript.

o Lines 538-544: A three-gene system is mentioned, but only two AmmoMemoRadiSam trees are found.

This part has been removed while streamlining the manuscript.

• Supplementary file 6: I find it difficult to find the proteins discussed in the text, for example "the biosynthesis of p-cresol from tyrosine (line 254-255)".

Abbreviations identifying the different enzymes have now been added to all mentions in the text, facilitating their localization in the supplementary file: "P. pyriformis encodes a complete pathway required for the biosynthesis of p-cresol from tyrosine (Supplementary file 6), only the second reported eukaryote with such capability. This pathway consists of three steps of the Ehrlich pathway (Hazelwood et al. 2008) converting tyrosine to 4-hydroxyphenyl-acetate (AAT, HPPD, ALDH) and the final step catalyzed by a fusion protein comprised of 4-hydroxyphenylacetate decarboxylase (HPAD) and its activating enzyme (HPAD-AE)."

• Supplementary file 11: Which group of species are highlighted in red? How do I know from which species these sequences are (I can make educated guesses, but prefer full species names). I do not find any reference to this file in the main manuscript.

We apologise for this inconvenience. The taxon labels in the treed in this supplementary file have been corrected to contain full species names.

Line 227-228: "630 OGs seem to be oxymonad-specific or divergent, without close BLAST hits". It is unclear if BLAST searches includes only a representative of each 630 OGs, or every single protein in these OGs.

The BLAST searches include every single protein in the investigated OGs. We clarified it in the text: “Of these, 630 OGs seem to be oxymonad novelties or divergent ancestral genes, without close BLAST hits (e-value -15) to any of these sequences.”

Line 243: I think it is five LGT mapped to internal nodes of Preoxystyla in Figure 1 (1+3+1).

You are correct, we apologize for the mistake. The sentence has been changed to: "Also, 46 LGT events were mapped to the terminal branches and 5 to internal nodes of Preaxostyla, suggesting that the acquisition of genes is an ongoing phenomenon, and it might be adaptive to particular lifestyles of the species."

Lines 325-331: The argument would be stronger with a figure showing the fusion and the alignment indicating the conserved amino acids mentioned in the text.

We agree with the reviewer but for the sake of space, we finally decided not to include a new figure.

Lines 425: "none of the species encoded" should be replaced by something like "none of the enzyme could be detected in any of the species" (the datasets are incomplete).

The sentence has been changed to: "None of the alternative enzymes mediating the conversion of pyruvate to acetyl-CoA, pyruvate:NADP+ oxidoreductase (PNO) and pyruvate formate lyase (PFL), could be detected in any of the studied species."

Line 455: "suggesting a cytosolic localization of these enzymes in Preaxostyla." The absence of a phylogenetic affiliation with the S. salmonicida homolog does not preclude a MRO localisation.

The sentence was changed to: "Phylogenetic analysis of Preaxostyla ACSs (Supplementary file 4 B) shows four unrelated clades, none in close relationship to the S. salmonicida MRO homolog, consistent with our assumption that these enzymes are cytosolic in Preaxostyla."

Lines 570-571: "Manual verification indicated that all the candidates recovered in oxymonad data sets are false positives" Using which criteria?

The manual verification was based on the annotation of predicted proteins by BLAST and InterProScan. If the annotations did not correspond to the suggested function, they were considered false positives. For example, the protein BLNAU_15573 of Blattamonas nauphoetae was detected by Sam50 HMM profile and thus was considered a candidate for Sam50 proteins. Its functional annotation from BLAST was, however, unrelated to Sam50 (“putative phospholipase B”). Therefore, this candidate was concluded as a false positive hit of the HMM search resulting from the very high sensitivity of this method.

We clarified this in the Results

“Reciprocal BLASTs indicated that all the candidates recovered in oxymonad data sets are very likely to be false positives based on the annotations of their top BLAST hits (mainly vaguely annotated kinases, peptidases and chaperones) (Fig. 6, Supplementary file 9).”.

And Material and Methods

“Any hits received by the methods described above were considered candidates and were furter inspected as follows. All candidates were BLAST-searched against NCBI-nr and the best hits with the descriptions not including the terms 'low quality protein', 'hypothetical', 'unknown', etc. were kept. For each hit, the Gene Ontology categories were assigned using InterProScan-5.36-75.0. If the annotations received from BLAST or InterProScan corresponded to the originally suggested function, the candidates were considered as verified. Otherwise, they were considered as false positives.”

Lines 743-755: "Similar observations were made in other protists with highly reduced mitochondria, such as G. intestinalis or E. histolytica,..." References are needed.

This part of the manuscript has been removed while streamlining the text.

Line 849: How was the manually curation done for the gene models in the training set?

The sentence has been changed to: "For de novo prediction of genes, Augustus was first re-trained using a set of gene models manually curated with regard to mapped transcriptomic sequences and homology with known protein-coding genes."

Lines 853-856: It is a bit unclear which dataset was used for BUSCO and downstream analysis. Was it the Augustus-predicted proteins, or the EVM polished?

The sentence has been changed to: "The genome completeness for each genome was estimated using BUSCO v3 with the Eukaryota odb9 dataset and the genome completeness was estimated on the sets of EVM-polished protein sequences as the input."

Lines 858: What is it meant that KEGG and similarity searches was used in parallel (what if both gave a functional annotation?)?

A sentence has been added for clarity: "KEGG annotations were given priority in cases of conflict."

Lines 861-862 and 1007-1008: Which genes or sub-projects does this apply to? How many genes were detected in this procedure?

The sentence has been changed to make this clear: "Targeted analyses of genes and gene families of specific interest were performed by manual searches of the predicted proteomes using BLASTp and HMMER (Eddy 2011), and complemented by tBLASTn searches of the genome and transcriptome assemblies to check for the presence of individual genes of interest that were potentially missed in the predicted protein sets (single digits of cases per set). Gene models were manually refined for genes of interest when necessary and possible."

Lines 878-879: It is not clear to me why the sum of the two described numbers should be as high as possible and would appreciate an argument or a reference.

When optimizing the inflation parameter of OrthoMCL, we reasoned that the optimal level of grouping/splitting for our purpose should result in the highest number of orthogroups containing all representatives of the groups of interest (i.e. Preaxostyla) but no other species – pan-Preaxostyla orthogroups. When going down with the values, you observe more and more groupings of pan-Preaxostyla OGs with others (indication of overgrouping) in the opposite direction you observe splitting of pan Preaxostyla OGs which indicates oversplitting. Because we were optimizing the inflation parameter for Preaxostyla and Oxymonadida at the same time, we maximized the sum of pan-Preaxostyla and pan-Oxymonadida groups.

Lines 879-881: "Proteins belonging to the thus defined OGs were automatically annotated using BLASTp searches against the NCBI nr protein database (Supplementary file 1)." Why were these annotated in a different way (compare lines 857-859).

This little inconsistency resulted from the fact that these parts of the analyses were performed by different researchers who did not cross-standardize the procedures. This inconsistency has no effect on the downstream analyses and conclusions as the annotations from Supplementary file 1 were not used in any further analyses.

Lines 894-957: "Detection of lateral gene transfer candidates": • It is not clear which sequences were tested in the procedure. All Preaxostyla, or all metamonada? I think I am confused because in the result sections you only report numbers for Preaxostyla, but in the method section metamonada is mentioned repeatedly.

Thank you for noticing. There was indeed some inconsistency in our writing.

We did an all-against-all search using all metamonads. However, we filtered out all homologous families in which Preaxostyla were not present or that had no hit against GTDB. So in the end, the LGT search was restrained to protein families containing Preaxostyla homologues. We corrected the wording in our method section.

• It would be easier to follow the procedure if numbers are provided for the different steps.

We are not sure what numbers the reviewer refers to here.

• Why was only small oxymonad proteins discarded (line 900)?

This is indeed a mistake. We meant “Preaxostyla proteins”. This is because we only considered Preaxostyla sequences with significant hits against GTDB as a starting point, so we aimed to first remove those that might be too short to yield reliable phylogenies.

• Line 911: How many sequences were collected?

Up to 10,000 hits were retained. We have added that information to the text.

• Lines 916-919: What is the difference between the protein superfamilies (line 916) and the OGs (line 919)? Are the OGs the same orthogroups that is described earlier in the method section? How are the redundancy of NCBI nr entries retrieved in different searches dealt with?

We understand the confusion here. It primarily stemmed from two different ways to establish homologous families across the manuscript because of different researchers being responsible for different parts. Protein superfamilies that were used for reconstructing the single protein trees used for the LGT analyses were assembled based on the procedure describe line 916-919 (“Protein superfamilies were assembled by first running DIAMOND searches of all metamonad sequences against all (-e 1e-20 --id 25 --query-cover 50 --subject-cover 50). Reciprocal hits were gathered into a single FASTA file, as well as their NCBI nr homologues.”). However, this was a somewhat stricter procedure than the one used to establish the OGs that are discussed in the rest of the manuscript (because of the e-value and identity cut-off used), so we eventually enriched the datasets with the putatively missing metamonad sequences that were present in the OGs but not in the initial superfamily assembly. However, since these were often more divergent sequences, we did not use these as queries for our BLAST searches against prokaryotes.

Line 987-989: "...was facilitated by Rsg1 being rather divergent from other Ras superfamily members" This statement is vague. What does it mean in practise?

The sentence has been changed to: " The discrimination was facilitated by Rsg1 having low sequence similarity to other Ras superfamily members (such as Rab GTPases)."

Lines 1037-1038: Why were these proteins re-annotated?

They were not. We are sorry for this mistake, which has been fixed in the revised manuscript.

Figures: The figures would be easier to follow if the colour coding for the five different species were consistent between the figures.

This is a good point, the colour coding has been unified across all figures.

Figure 1: It appears that the Venn diagram in C only shows the Preaxostyla-specific protein in B, not all OGs for which contain Preaxostyla proteins. This is not clear from legend or from the figure itself. The same comment applies to D.

The interpretation of the figure by the reviewer is correct; we have modified the legend to make the meaning of the figure easier to understand.

Figures 2 and 6: It would be clearer with panel labels A, B, etc, instead of "upper" and "lower" panel, as in the other figures.

This is a fair point, we have added the alphabetical labels proposed by the reviewer to the figures.

Figure 6: What is the colour code in the figure? The numbers within the boxes are not aligned.

We have added an explanation of the color code to the legend and edited the figure to make it aesthetically more pleasing.

Supplementary figures 1-3: What do green and magenta indicate in the figure?

As with the previous figure, the color code is now explained in the revised legend.

** Referees cross-commenting** I agree with the other reviewers that the discussion of the functional and ecological implications of the LGTs could be developed.

We understand the reviewers but as already explained in response to Reviewer 1, we have decided not to extend the already rather long manuscript further. We believe that the several exemplar LGT cases that we do discuss in detail provide a good impression of the significance of LGT in the evolution of Preaxostyla.

In contrast to reviewer 2, I do not see that the authors discuss their result in the context of eukaryogenesis in this manuscript. Maybe the reference reviewer 2 mention could be cited in the introduction together with Hampl et al. 2018 to acknowledge that there are different views about the importance of secondarily amitochondrial eukaryotes on our thinking about the origin of eukaryotes. I disagree with reviewer 2's objection against the wording "... and undergo pronounced morphological evolution" because I think Fig. 4 in Hampl 2017 shows a large morphological diversity among oxymonads.

We are glad to see that our perspective is not shared by other colleagues in the field. Nevertheless, having carefully considered the case we have decided to remove any mentions of eukaryogenesis from the revised manuscript, as we admit this topic is peripheral to the key message of our present study. On the other hand, we appreciate very much the note by the reviewer on the large morphological diversity among oxymonads – we have now added a similar remark to the revised manuscript (the last sentence of Conclusions).

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Referee #2

Evidence, reproducibility and clarity

Using draft genome sequencing of the free-living Paratrimastix pyriformis and the sister lineage oxymonad Blattamonas nauphoetae, Novack et al. infer the metabolic potential of the two protists using comparative genomics. The authors conclude that the common oxymonad ancestor lost the mitochondrion/mitosome and discuss general strategies for adapting to commensal/symbiotic life-style employed by this taxon. Some elaborations on pathways go on for several paragraphs and feel unnecessarily stretched, which made those sections of the paper rather difficult to digest. This might be also be because the work, and all conclusions drawn, depend entirely on incomplete (ca. 70-80%) genome data and simple similarity searches, and e.g. no kind of biochemistry or imaging is presented to underpin the manuscripts discussion. This is noteworthy in light of other protist genome reports published in the last few years that differ in this respect, including previous work by this group. And for sequencing-only data, this paper - https://doi.org/10.1016/j.dib.2023.108990 - might offer an example of where we are at in 2023. With respect to previous work of the group (Karnkowska et al. 2016 and 2019), this submission is very similar (analysis pattern, even some figures and more or less the conclusion), i.e. to say, the overall progress for the broader audience is rather incremental. Then there are also some incidents, where the data presented conflicts with the authors own interpretation. The text (including spelling and grammar) needs some attention and the choice of words is sometimes awkward. The overuse of quotation marks ("classical", "simple", "fused", "hits", "candidate") is confusing (e.g. was the BLAST result a hit or a "hit").

In its current form the manuscript is, unfortunately, very difficult to review. This reviewer had to make considerable efforts to go through this very large manuscript, mainly because of issues affecting to the presentation and the lack of clarity and conciseness of the text. It would be greatly appreciated if the authors would make more efforts upfront, before submission, to make their work more easily accessible both to readers and facilitate the task of the reviewers.

About a fifth of the two genome is missing according the authors prediction (table 1). Early on they explain the (estimated) incompleteness of the genomes to be a result from core genes being highly divergent. In light of this already suspected high divergence, using (the simplest NCBI) sequence similarity approach to call out the absence of proteins (for any given lineage) may need lineage-specific optimization. The use of more structural motif-guided approaches such as hidden Markov models could help, but it is not clear whether it was used throughout or only for the search for (missing) mitochondrial import and maturation machinery. The authors state that the low completeness numbers are common among protists, which, if true, raises several questions: how useful are then such tools/estimates to begin with and does this then not render some core conclusions problematic? The reader is just left with this speculation in the absence of any plausible explanation except for some references on other species for which, again, no context is provided. Do they have similar issues such as GC-content, same core genes missing, phylogenetic relevance?, etc.. No info is provided, the reader is expected to simply accept this as a fact and then also accept the fact that despite this flaw, all conclusions of the paper that rests on the presence/absence of genes are fine. This is all odd and further skews the interpretations and the comparative nature of the paper.

As a side note, this will also influence the number of proteins absent in other lineages and as such has consequences on LGT calls versus de novo invention. For the cases with LGT as an explanation, it would help to briefly discuss the candidate donors and some details of the proteins in the eco-physiological context (e.g. lines 263-268 suggest that HPAD may have been acquired by EGT which was facilitated by a shared anaerobic habitat and also comment on adaptive values for acquiring this gene). Exchanging metabolic genes via LGT (Line 163) blurs the differences between roles and extent of LGT in prokaryote vs eukaryote, and therefore is exciting and could use support/arguments other than phylogenies. I guess the number of reported LGTs among protists (whatever the source) over the last decade has by now deflated the novelty of the issue in more general; a report of the numbers is expected but they alone won't get you far anymore in the absence of a good story (such as e.g. work on plant cell wall degrading enzymes in beetles). It would help to clarify which parts of the mitochondrial ancestor were reduced during the process of reductive evolution at what time in their hypothesized trajectory. For instance, loosing enzymes of anaerobic metabolism conflicts with the argued case of an aerobic (as opposed to facultative anaerobic) mitochondrial ancestor followed by gains of anaerobic metabolism in the rest of the eukaryotes via LGT, and some papers the authors themselves cite (e.g. the series by Stairs et al.). There is no coherent picture on LGT and anaerobic metabolism, although a reader is right to expect one.

In light of their data the authors also discuss the importance of the mitochondrion with respect to the origin of eukaryotes:

First, the mitochondrion brought thousands of genes into the marriage with an archaeon, surely hundreds of which provided the material to invent novel gene families through fusions and exon shuffling and some of which likely went back and forth over the >billion years of evolution with respect to localizations. The authors look at a minor subset of proteins (pretty much only those of protein import, Fig. 6) to conclude, in the abstract no less: „most strikingly the data confirm the complete loss of mitochondria and every protein that has ever participated in the mitochondrion function for all three oxymonad species." I do not question the lack of a mitochondrion here, but this abstract sentence is theatrical in nature, nothing that data on an extant species could ever proof in the absence of a time machine, and is evolutionary pretty much impossible. A puzzling sentence to read in an abstract and endosymbiont-associated evolution.

Second, using oxymonads as an example that a lineage can present eukaryotic complexity in the absence of mitochondria and conflating it with eukaryogenesis is a logical fallacy. This issue already affected the 2019 study by Hampl et al.. We have known that a eukaryote can survive without an ATP-synthesizing electron transport chain ever since Giardia and other similar examples and the loss of Fe-S biosynthesis and the last bit of mitosome (secondary loss) doesn't make a difference how to think about eukaryogenesis. It confuses the need and cost to invent XYZ with the need and cost of maintenance. How can the authors write "... and undergo pronounced morphological evolution", when they evidently observe the opposite and show so in their Fig. 1? The authors only present evidence for reductive evolution of cellular complexity with the loss of a stacked Golgi. What morphological complexity did oxymonads evolve that is absent in other protists? A cytosolic metabolic pathway doesn't count in this respect, because it is neither morphological, nor was it invented but likely gained through LGT according to the authors. This is quite confusing to say the least. A recent paper (https://doi.org/10.7554/eLife.81033) that refers to Hampl et al. 2019 has picked this up already, and I quote: "Such parasites or commensals have engaged an evolutionary path characterized by energetic dependency. Their complexity might diminish over evolutionary timescale, should they not go extinct with their hosts first." Here the authors raise a red flag with respect to using only parasites and commensals that rely on other eukaryotes with canonical mitochondria as examples. If we now look at Fig. 1 of this submission, Novak et al. underpin this point perfectly, as the origin of oxymonads is apparently connected to the strict dependency on another eukaryote (or am I wrong?), and they support the prediction with respect to complexity reducing after the loss of mitochondria - mitosome gone, Golgi almost gone. What's next? This is a good time to remember that extant oxymonads are only a single picture frame in the movie that is evolution, and their evolution might be a dead-end or result in a prokaryote-like state should they survive 100.000s to millions of years to come.

Some more thoughts:

Line 47-52: Hydrogenosome or mitosome is a biological and established label as (m)any other and I find the use of the word "artificial" in this context strange. While the authors are correct to note that there is a (evolutionary) continuum in the reduction - obviously it is step by step - they exaggerate by referring to the existing labels as "artificial". You make Fe-S clusters but produce no ATP? Well, then you're a mitosome. It's a nomenclature that was defined decades ago and has proven correct and works. If the authors think they have a better scheme and definition, then please present one. Using the authors logic, terms such as amyloplast or the TxSS nomenclature for bacterial secretions systems are just as artificial. As is, this comes across as grumble for no good reason.

Line 158: A duplication-divergence may also explain this since sequence similarity-based searches will miss the ancestral homologues.

Lines 201-202: Presence of GCS-L in amitochondriate should be explained in light of this group once having a mitochondrion, which then makes ancestral derivation and differential loss (as invoked for Rsg1) also a likely explanation along with eukaryote-to-eukaryote LGT.

Lines 356-392: Describes plenty of genomic signal for Golgi bodies but simultaneously cites literature suggesting the absence of a morphologically an identifiable Golgi in oxymonads. An explicit prediction regarding what to observe in TEM for the mentioned species might be nice to stimulate further work.

Lines 414: The preceding paragraphs in this result section describes only the distribution, without mentioning origins - a sweeping one-line summary that proclaims different origin needs some context and support. Furthermore, the distribution of glycolytic enzymes might indeed be patchy, but to suggest it represents an 'evolutionary mosaic composed of enzymes of different origins' without discussing the alternative of a singular origin and different evolutionary paths (including a stringer divergence in one vs. another species) discredits existing literature and the authors own claim with respect to why BUSCO might fail in protists.

Line 486: How uncommon are ADI and OTC in lineages sister to metamonada?

Line 504: It might help an outside reader to include a few lines on consequences and importance of having 2Fe-S vs 4Fe-S clusters and set an expectation (if any) in Oxymonads

Any explanations on what unique selection pressures and gene acquisition mechanisms may be operating in P. pyriformis which might allow for the unique metabolic potential?

** Referees cross-commenting**

To R3: Hampl et al. 2019, to which Novak et al. refer, is about eukaryogensis and that is exactly the context in which this is discussed again and what Raval et al. 2022 had decided to touch upon. If the authors do not bring this up in light of the ability to evolve (novel) eukaryote complexity, then what else? Maybe they can elaborate, especially with respect to energetics to which they explicitly refer to in 2019 (and here). And with respect to text-book eukaryotic traits (and the evolution of new morphological ones), I do not see any new ones evolving in any oxymonad, but reduction as Novak et al. themselves picture it in this submission. Is a change in the number of flagella pronounced morphological evolution? Maybe for some, but I believe this needs to be seen in light of the context of how they discuss it. I see a reduction of eukaryotic complexity and not a gain. They have an elaborate section on the loss of Golgi characteristics (and a figure), but I fail to read something along the same lines with respect to the gain of new morphological traits. Again, novel LGT-based biochemistry does not equal the invention of a new morphology such as a new compartment. Oxymonads depend on mitochondria-bearing eukaryotes for their survival or don't they? This is the main point, and if evidence show that I am wrong, then I will be the first to adapt my view to the data presented.

I have concerns with the presentation of a narrative that in my opinion is too one-sided and that has been has been publicly questioned in the community (in press, at meetings, personally). For the benefit of science and of the young authors on this study, this reviewer feels strongly that these issues should be taken very seriously and discussed openly in a more balanced way. . We only truly move forward on such complex topics, if we allow an open and transparent discussion.

Having said that, I am happy that R3 has picked up exactly the same major concerns as I did with respect to e.g. the phrasing on mito (gene) loss and the BUSCO controversy.

Significance

Using draft genome sequencing of the free-living Paratrimastix pyriformis and the sister lineage oxymonad Blattamonas nauphoetae, Novack et al. infer the metabolic potential of the two protists using comparative genomics. The authors conclude that the common oxymonad ancestor lost the mitochondrion/mitosome and discuss general strategies for adapting to commensal/symbiotic life-style employed by this taxon. Some elaborations on pathways go on for several paragraphs and feel unnecessarily stretched, which made those sections of the paper rather difficult to digest. This might be also be because the work, and all conclusions drawn, depend entirely on incomplete (ca. 70-80%) genome data and simple similarity searches, and e.g. no kind of biochemistry or imaging is presented to underpin the manuscripts discussion.

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Reply to the reviewers

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

This study evaluates the effect of fungal toxin candidalysin on neutrophils. The authors show that candidalysin induces NETosis when secreted by hyphae, but when candidalysin is added on its own, NLS are formed instead which are distinct from NETs. The authors have done lots of carefully controlled experiments, and delineated key components of the pathway inducing NLS, including the role of ROS and histone modifications. The data provided is high quality and well presented in figures.

Reviewer #1 (Significance (Required)):

Strengths are the depth of analysis - many different aspects of NETosis is assessed and robustly tested.

Comments: 1. I was a bit confused by what should be the main message of the paper - is it that candidalysin on its own doesn't induce NETosis but only NLS? The answer to this question wasn't well addressed in my opinion, but the paper switches between using live fungi and purified candidalysin so it became confusing at times.

*

Responses:

Thank you for this important comment. We have clarified our narrative on candidalysin throughout the manuscript to provide a red thread for the readership. Our message is that candidalysin alone has not the capacity to induce a full cycle of signalling events which result in canonical NET formation. Our data show that candidalysin alone falls short and can only produce NLS. On the other hand, our data show that in the context of growing C. albicans cells candidalysin is able to promote the release of NETs. This is important, since previously the hyphal form of C. albicans has been reported to be a formidable inducer of NETs, whereas the yeast form was not. Our data put candidalysin in the centre of this observation, showing that it indeed is a major contributor to NET formation when present with growing C. albicans cells. Since candidalysin expression and release is strictly connected to hyphal growth our new data agrees with previous assessment and provides new insight in how this hyphae-specific inductive effect is accomplished.

In the revised manuscript, at first, we describe the difference of neutrophil stimulation when using strains expressing and lacking candidalysin as compared to candidalysin stimulation alone. We added or modified the following phrases:

• Line (163) “As candidalysin-expressing C. albicans strains induced more NETs than candidalysin-deficient strains, we investigated the role of the toxin alone in stimulating neutrophil extracellular trap release”.
• Line (173) “In order to ensure consistency in NET/NLS quantification, NLS were quantified with the same criteria as previous described for NETs.”

• Line (182) “In summary, candidalysin alone triggers morphologically distinct NLS in a time- and dose-dependent manner, whereas candidalysin-producing C. albicans hyphae induce canonical NETs (Fig. 1a).” Next, we describe the different morphology of NLS triggered by candidalysin alone in comparison to canonical NETs triggered by C. albicans strains expressing candidalysin. We added or modified the following phrases:

• Line (198) “To investigate candidalysin-triggered NLS in further detail, we used scanning electron microscopy (SEM) that allows a more detailed view of the neutrophil-derived structures (Fig 3a).” Furthermore, to prevent switching between experiments using candidalysin alone and experiments with different Candida strains, we have moved the next paragraph “Candidalysin-expressing strains induce more NETs and higher citrullination levels than candidalysin-deficient strains” to the end of the result section (old Fig. 4 is now new Fig. 8). In doing so, we focus on the direct morphological, signalling and functional effects of candidalysin alone on neutrophils and towards the end, we analyse how the strains are affected by different neutrophil killing mechanisms (phagocytosis and NETs). Subsequently, we synthetize our findings by showing that candidalysin is the main driver of histone citrullination by quantifying this histone modification in the context with NET induction comparing candidalysin-expressing and -deficient strains. We conclude that citrullination-induced chromatin decondensation in combination with candidalysin-induced ROS production are most probably the main contributors of increased NET formation stimulated by C. albicans hyphae expressing candidalysin. This is the also a good conclusion of the manuscript showing that candidalysin alone is not enough but together with growing C. albicans cells it contributes to NET induction and increased NETs in turn inhibit growth and limit spreading of C. albicans.

• We modified and added the following sentences to the discussion section: (line 457) “The data suggests that candidalysin is the key driver of histone citrullination in neutrophils infected with C. albicans and that addition of evenly distributed, external candidalysin in high concentration (15 µM) drives neutrophils towards NLS despite the presence of C. albicans cells. We conclude that, during infection, candidalysin-triggered Ca2+ influx and histone hypercitrullination amplify processes in neutrophils which are induced by C. albicans hyphae. These amplified processes culminate in a strongly increased release of NETs that in turn are formidable weapons to control hyphal filaments.”

  *2. If candidalysin on its own only induces NLS - what is the relevance of this for disease? A lot of work has been provided on the pathway driving NLS formation, but it wasn't clear to me why this is important. More in discussion needed or evidence of disease relevance. *

Responses:

Thank you for giving us the opportunity to clarify this issue. Candidalysin expression strongly increases with and is restricted to hyphal growth, which is the adhesive growth form of C. albicans. Given that epithelial cells expunge candidalysin for their own protection while hyphae remain attached, it could be possible that neutrophils get exposed to candidalysin before they encounter C. albicans cells. Therefore, it is relevant to understand how candidalysin per se shapes neutrophil responses. We have added the following sentences to the discussion section: (line 527) ”As epithelial cells are able to expunge candidalysin for protection while C. albicans hyphae remain adeherent 46 recruited neutrophils may encounter candidalysin before direct contact with hyphae.”

With regard to relevance for candidiasis the observation that candidalysin-deficient strains are poor inducers of NETs is most important. Since candidalysin expression is entirely restricted to hyphal growth. this finding gives crucial, new insight into the previous observation that hyphae are better NET inducers than yeast from C. albicans. In this context, we wanted to make it very clear to the reader that this effect only works when C. albicans cells and candidalysin are combined and that candidalysin alone does not lead to full-blown NET formation. Therefore, we have included a thorough investigation of the effects of candidalysin on neutrophils to be able to better contextualize our findings comparing candidalysin-expressing and candidalysin-deficient strains.

To make this point clearer. we added the following sentence to the summary at the end of the discussion section: (line 565) “Neutrophils encountering candidalysin-expressing hyphae are able to adequately respond by releasing increased amounts of NETs whereas secretion of candidalysin does not allow hyphae to evade from neutrophil attack.”

In addition, we are convinced that the move of former Fig.4 to the end of the result section (now Fig. 8) additionally helps the reader to better understand the importance to first delineate the effect of candidalysin on neutrophils alone and then to conclude the manuscript with experiments using different C. albicans strains to put the findings into context.

To add more substance to our conclusions we wrap up the new version of the manuscript with data comparing wild-type and candidalysin-deficient strains in neutrophil antimicrobial assays and quantification of histone citrullination. With the newly added antimicrobial assays we demonstrate that candidalysin expression does not affect phagocytic killing (Fig. 7d and 7e) as assessed by plating assays and that candidalysin does not affect inhibition by PMA-induced NETs (Fig. 7f and 7g). Thus, as stated above, during the interaction of hyphae and neutrophils candidalysin promotes the release of more NETs, but does otherwise not affect anti-Candida activity by neutrophils. Increased NETs in turn, however, inhibit growth and limit spreading of C. albicans. The manuscript now ends with the data on differences in histone citrullination when using wild-type and candidalysin-deficient strains indicating that citrullination-induced chromatin decondensation in combination with C. albicans cells ultimately leads to increased NET release.

We added the following text to the manuscript: (Line 416) “To corroborate, whether candidalysin deficiency affects C. albicans’ susceptibility to neutrophil attack we performed two antimicrobial assays. In the first assay we determined NET-mediated anti-Candida activity by preformed NETs comparing wild-type and candidalysin-deficient strains. We used the same imaged-based analysis with calcofluor white staining. To be able to better observe differences in susceptibility of the different strains we used a slightly higher MOI than for the previous NET inhibition assays which explains higher survival percentage (Fig. 7c, black bars on the right side). As expected, candidalysin did not affect the inhibitory effect on C. albicans imposed by NETs (Fig. 7c). In the second assay, we determined short-term anti-Candida activity of intact neutrophils, which is predominantly phagocytic elimination, by serial dilution and plating for colony counts. Candidalysin-deficient and wild-type strains are killed similarly over the time of 1 to 4 h, both at MOI 1 and 3 (Fig. 7d and 7e). This indicates that candidalysin expression does not enable evasion from neutrophil phagocytic attack and this result agrees well with our previous finding that wild-type C. albicans engulfed by human neutrophils are unable to escape by hyphal outgrowth 16. In conclusion, while candidalysin strongly increases the NET-inductive capacity of C. albicans hyphae, the toxin does neither affect the anti-Candida effect of intact neutrophils nor of NETs.”

Notably, it is not informative to use C. albicans as inducer of NETs and as target of anti-Candida activity by NETs in the same assay, since both induction and anti-Candida activity are dependent on the amount of C. albicans cells. We therefore chose to show two separate assays where we (i) quantify short-term killing by plating (mainly phagocytosis) and (ii) quantify growth inhibition of C. albicans by pre-stimulated NETs.

*3. In Figure 2, it would be helpful to include images of ionomycin-stim neutrophils for comparison of the NLS structures across different stim conditions. *

Response:

This is a very good point. We supply a structural comparison between NLS and NETs induced by PMA, ionomycin and candidalysin in Figure 3. Additionally, the time-dependent changes for ionomycin are now included in the supplementary Figure S1.

4. Few places where reference manager has failed (see bottom on page 10, line 190 for example)

Response:

We have fixed this issue, thank you for pointing it out.

*5. Lines 191-198 - I was confused here by the text. I thought the point was that candidalysin induced NLS similar to ionomycin, but here the point is being made that the two are different? This led me to being confused as to the point of all the comparisons made between ionomycin NLS and candidalysin NLS... this could be made clearer. *

Responses:

Thank you for highlighting this. According to previous literature ionomycin, a bacterial peptide toxin, was the most prominent example for induction of leukotoxic hypercitrullination. Therefore, we used ionomycin to put our findings with candidalysin, a fungal peptide toxin, into context. We find that candidalysin share similarities but also some striking differences to ionomycin. While we could not investigate the nature of these differences in more detail, this could be the basis of a follow-up study, we think it is important to give the reader the comparison in order to better understand how candidalysin shapes neutrophil responses. One clear difference which we show in the manuscript is that candidalysin induces some ROS whereas ionomycin does not at all (Fig. 4).

We changed the text in the result section accordingly to make our point clearer: (line 203) “PMA exposure generated widespread chromatin fibers in the extracellular space (Fig. 3a, left panels) whereas ionomycin exposure resulted in more compact, patchy areas occasionally dispersed with long, thin chromatin fibres (Fig. 3b, middle panels). With regard to morphological changes, candidalysin treatment resulted in compact, fibrous structures resembling those stemming from ionomycin treatment, however long, thread-like structures were absent in candidalysin-treated neutrophil samples (Fig. 3a right panels, for 7 h treatment see Fig. S1c).”

And did so as well in the discussion section: (Line 513) ”While ionomycin- and candidalysin-induced NLS shared similar key features, such as increased histone citrullination, our study revealed striking differences between the two toxins. In contrast to ionomycin, candidalysin stimulation led to ROS production in neutrophils.”

*6. Could the authors include some unstim neutrophil control images in Fig 3 for the SEM? Can the SEM sample processing affect neutrophil structure in anyway? Feels like an important control although I don't have much experience with SEM personally *

Response:

This is of course a relevant control image. We have included an image showing unstimulated neutrophils from similar time points, but without exposure to candidalysin (Fig. 3). The unstimulated neutrophils are spherical and morphologically distinctly different from candidalysin-treated neutrophils.

*7. I was very intrigued by the experiments where the authors added candidalysin in to neutrophils infected with ece1-null strain. Those experiments showed that candidalysin addition still drove NLS instead of NETosis. Can the authors investigate why this is? Is membrane intercalation different when candidalysin is delivered by hyphae vs added on its own? Could that explain some of the differences they have seen? *

Responses:

Thank you for this comment. Yes, there is a clear difference, since we add candidalysin to the medium such that the peptide is evenly distributed and reaches membranes rather evenly from the extracellular space. When released from growing C. albicans hyphae candidalysin is then predominantly released on hyphal tips as demonstrated in the referenced article (doi.org/10.1111/cmi.13378). Hyphal tips in turn are readily attacked by human neutrophils (doi.org/10.1189/jlb.0213063). Hence, we can safely assume according to these previous publications that there will be a more uneven distribution of candidalysin concentrations over neutrophil membranes, when the sole source of the toxin stems from growing hyphae interacting with neutrophils. It would of course be very interesting to know how the toxin exactly intercalates into membranes and which morphologies potential pores may have. These questions are currently under investigation in the laboratories of Profs Hube and Naglik. To include these findings here would certainly be far beyond the scope of this study.

We include and modify the following sentences to the discussion of this manuscript to clarify the issue: (Line 541). ”One of the main goals of the study was to delineate contribution of candidalysin to neutrophil responses either as factor released by C. albicans hyphae or as singular peptide toxin. Our data demonstrates that candidalysin is the main driver of histone citrullination in neutrophils infected with C. albicans (Fig. 8). Lack of candidalysin production in C. albicans results in significantly reduced histone citrullination, accompanied with decreased NET formation. However, citrullination is not required for NET release, but rather governs the formation of NLS, which is dominant when candidalysin is added exogenously with even distribution throughout the cell suspension. With regard to C. albicans hyphae secreting candidalysin, local concentrations of the toxin are likely to vary to a large degree, particularly when the candidalysin-secreting hypha is engulfed by a neutrophil. Therefore, it may be difficult to discriminate NLS form NETs during the interaction of neutrophils and C. albicans, as both structures may be induced concurrently 10. It seems logical that the pore-forming activity of candidalysin augments the release of NET fibres during C. albicans infection, where PRRs will additionally be triggered on neutrophils, resulting in combinatorial activation of downstream pathways. In line with this notion, candidalysin drives histone citrullination, which contributes to chromatin decondensation.”

*8. Is phagocytosis needed for NETosis induction by candidalysin? What happens if you add beads or beta-glucan particles with candidalysin stimulation? Do you get NLS or NETs? *

Responses:

This is an interesting question. Physical contact is required for the induction of NET formation (10.1111/j.1462-5822.2005.00659.x, 10.1371/journal.ppat.1000639) and physical contact leads to pattern recognition unequivocally followed by phagocytic events in neutrophils. Hence, at the least indirectly, phagocytosis and NET formation are connected, but may not be so causally.

While glucan-covered particles have been shown to induce NETs (10.1159/000365249), we show that C. albicans cells devoid of candidalysin induce NETs, but to a much lesser extent than wild-type C. albicans. In addition, the experiment shown in Fig. 8 shows exactly that. Instead of glucan-covered beats we used C. albicans cells (Fig. 8f) which by virtue are glucan covered.

*9. Please confirm what the n numbers refer to in the figure legends - are these biological or technical replicates? How many experiments are the representative images representing? *

Response:

Thank you very much for pointing this out. We adapted our figure legends accordingly and added the number of biological and technical replicates (n=x(y), x=biological replicates, y=technical replicates). Each experiment has been performed with at least three biological replicates which includes the use of different neutrophil donors.

---

*Reviewer #2 (Significance (Required)):

*

*The advantage of this work is the presentation of the mechanism associated with NLS formation in contact with candidalysin, where activation of NADPH oxidase and calcium influx have been documented to be important. This toxin can trigger ROS production and activate downstream signaling that is important for morphological changes and NLS formation. The important finding is also that NLS are resistant to nuclease treatment and increase the ability of neutrophils to control C. albicans hyphae formation and fungal cell growth. These findings provide a better understanding of the role of neutrophils in the treatment of infections caused by these microorganisms. Below I present are minor suggestions that, in my opinion, will improve the text and correct the presentation of the results, making this set of results a valuable source for explaining such a complex problem.

*

Response:

Thank you for this assessment. In cases which we have identified as crucial for our message we have decided to include additional experiments to better convey our message (Fig. 6e-f and Fig. 7d-g). We also included a time course for ionomycin stimulation of neutrophils in Fig. S1. We appreciate that the overall assessment was that no additional experiments were required.

1/ The authors should decide what thesis about NLS they want to prove: 100 NLS are less fibrous and ....... than canonical NETs and are triggered in an NADPH oxidase-independent fashion.

* 121 NLS were dependent on NADPH oxidase-mediated reactive oxygen species (ROS) production

*

Response:

This was indeed imprecisely formulated from our side. NLS were previously described as NADPH-independent processes stimulated by toxins (see ionomycin). Candidalysin seems to trigger NADPH-dependent and NADPH-independent pathways. However, the main differentiation criteria were described through the hypercitrullination which we could observe for candidalysin. To clarify, we have modified the following sentence: (line 121) ”In contrast to previously described stimuli of NLS, candidalysin induced NLS in partial dependence on NADPH oxidase-mediated reactive oxygen species (ROS) production, wheras PAD4-mediated histone citrullination could be observed as well. Notably, candidalysin alone failed to induce NETs as indicated by a lack of cell cycle activation determined via lamin A/C phosphorylation assays.”

*2/ for the experiment described in the line below, MOI 2 was chosen; did the authors conduct an analysis of the response/eventual change in it, depending on the MOI?

*

Response:

Yes, from our experience in in vitro experiments with human neutrophils MOI3 C. albicans overgrows too quickly. This is why an MOI 1-3 is the best option to analyse NET induction capacities.

131 we infected neutrophils with wild-type C. albicans, ECE1-deficient (ece1ΔΔ), and corresponding revertant (ece1ΔΔ*+ECE1) strains,

3/ Has the effect of deletion of ECE1 on other aspects of virulence, such as adhesion, virulence factor production, or biofilm formation, been analyzed? *

Response:

Yes indeed, the effect of candidalysin on other aspects has been studied. Candidalysin has no effect on adhesion and is expressed during biofilm formation. It has a broad effect on virulence in general and promotes neutrophil recruitment indirectly by a robust induction of damages responses. To clarify the amount of studies investigating these other aspects and to pinpoint the knowledge gap for direct interaction of neutrophils and candidalysin we include the following sentence: (line 132) “C. albicans hyphae release candidalysin and while the effects of the toxin for instance on virulence in general and on adhesion to host cells have been widely studied 17,18,23,28,30, the direct impact of candidalysin on the neutrophil immune response towards C. albicans, remains poorly understood. To investigate the role of candidalysin, we infected neutrophils with wild-type C. albicans,…”

*137 the ECE1- and candidalysin-deficient strains triggered reduced levels

4/ Fig.1 - How were C. albicans cells stained? Does 100%NET mean the number of cells netting after PMA treatment? This information should be given.

*

Response:

Thank you for pointing this out. We were a bit unclear here. We added details in the respective figure legend and method section. C. albicans cells were visualised with anti-Candida antibody (1 µg/mL, ProSci, Cat#35-645). Furthermore, C. albicans nuclei are stained by DAPI, too. 100% NETs would mean that every single neutrophil (an image event which stains for neutrophil markers) in the analysed microscopic picture shows NET or NET-like morphology. We did not normalize to PMA treated cells.

5/ 168 dependent effect with increased NLS formation from 3 μM to 15 μ*M. However, the reduced NLS

How was determined the limiting concentration value of the toxin, for which an increase in NLS was observed? Was a wide range of concentrations used in the analysis or was the determination made only for these three selected values? A complete concentration analysis should be performed. *

Response:

This is of course a valid point. We showed data on these concentrations as established from previous studies of our collaborators (10.1111/cmi.13378; 10.1038/nature17625; 10.1038/s41467-019-09915-2). Under 3 µM we did not observe much measurable results and therefore omitted these. Concentrations above 70 µM did not change the outcome anymore than at 70 µM, so higher concentrations were omitted. We, thus, show 3µM at which we see mild effects, show 15 µM (a 5-fold increase compared to 3µM) at which we see profound effects and show 70 µM (again approximately a 5-fold increase compared to 15 µM) at which we see an overwhelming effect. Additional concentrations in between the applied concentration values would not add much new information.

6/ 169 formation was observed at 70 μ*M (Fig. 2b), which can be explained by neutrophil cell death induced by the toxin as determined by a DNA Sytox Green assay (Fig. S1a).

Was another viability test conducted? AnnexinV? Caspase 3/7? Sytox is not a specific staining in this regard. Furthermore, in Fig. S1a you state the kinetics of cell death, also after PMA treatment. On the one hand, you say that the production of candidalysin of NLS above 70 uM is reduced due to cell death, but at the same time you define as cell death the changes under PMA, which induce netosis. Please explain this reasoning better. *

Responses:

Thank you for pointing this out. We have no indication that candidalysin stimulates apoptosis in neutrophils. Therefore, no AnnexinV/Caspase 3/7 stain was performed. What we wanted to emphasize is that at 70 µM candidalysin the cytotoxic character of candidalysin is overwhelming leading to rather quick cell death, as assessed by the Sytox assay. Sytox is specific in the regard that it determines whether the plasma membrane is permeable and gives the stain access to the nuclear DNA to result in a positive signal. We use this assay to quantify NET formation, since it is a quantitative assay and less laborious than microscopy. However, we always back up NET assays with microscopic, image-based analyses and do not use the Sytox assay as standalone experiment for NET quantification, since the Sytox assay is not specifically staining netting cells, but it also stains other types of cell death.

We clarify this in the text as follows: (line 659) “Neutrophil cell death or the presence of extracellular DNA was quantified using a Sytox Green-based (Invitrogen) fluorescence assay similar to previous descriptions 2,35. To ultimately quantify NETs or NLS we always used image-based assys, the cell death assay was only used as complementation.”

*7/ 175 mixing of granular and nuclear components at ~120 min after stimulation (Fig. 2d and Fig. S2).

Figure S2 does not show mixing with the content of the granules. You are not labeling any granule component, only histones. You cannot draw that conclusion from these results. *

Response:

We respectfully disagree. As indicated in the figure legend for Figure 2d we were labelling for neutrophil elastase (red) which is located in azurophilic granules and thereby presents a marker for granular content. Since we wrongfully referred to Figure S2 here, we removed this from the text. The latter reference probably remained erroneously from a previous version.

*8/ Fig. 2. What concentration of PMA was used? What does 100% NLS mean? How is it different from 100% NET, since you are using PMA in both cases. Please explain. *

Responses:

We have now defined PMA concentration in the respective figure legend (100nM). The criteria for image-based assessment of NLS and NET quantification are the same for reason of comparison. PMA is included in each of the experiments as a positive control to show that the used neutrophils react upon stimulation. To clarify, we now specify at the y-axis %NETs or NLS. As stated above, 100% NLS means that each cell event in the image has increased in diameter such that it is considered as a NET or NLS. Hence, we use a common coordinate system to quantify extracellular events (NETs and NLS) based on size.

We have adjusted the figure legend as follows: (line 186) “Fig 2. Candidalysin induces ____NLS ____in human neutrophils. Candidalysin, but not scrambled candidalysin or pep2, another Ece1p-derived peptide (all 15 µM), induce (a) DNA decondensation in human neutrophils after 4 h (n = 4(10-14)) in a (b) dose-dependent manner (n = 3(10-14)). To allow comparability, NLS were quantified with the same criteria as previously described for NETs. Data shown as mean ± SEM. Confocal images (c) of immunostained cells display morphological changes involving nuclear and granular proteins after 4 h compared to unstimulated cells or 100 nM PMA, or cells exposed to scrambled candidalysin and pep2. The morphological changes evoked by PMA considerably deviate from morphological changes evoked by candidalysin and, hence, are defined as NETs (for PMA) and NLS (for candidalysin). Time-dependent progression of morphological changes (d) in neutrophils induced by candidalysin over the course of 5 h (all images are with 60X magnification).”

*9/ 181 NLS were quantified with the same criteria as previous described for NETs.

The criterion for NETs was an area above 100um2, so what is the criterion for NLS? If we assume that this is the same as for NETs, then what is the difference between NLS and NETs? The criteria adopted do not differentiate between the two forms and appear to be subjective. *

Responses:

As stated above, for us it was very important to find a common coordinate system to quantify NETs and NLS, since we wanted to deliver comparable and solid quantitative data. Hence, the quantification method does not discriminate between NETs and NLS. The notable morphological differences of NETs and NLS are thoroughly described with Figure 2 and Figure 3 and defined by differences in their structure. In addition, we present differences and similarities of induced pathways leading to canonical NETs or candidalysin-induced NLS in Figure 6 and Figure 7. We are convinced that, since NETs and NLS vary in size (DNA area covered), it will not be accurate for quantification purposes to include an additional size cut-off in the attempt to discriminate NLS and NETs. Instead we have established that candidalysin alone induces morphologically distinct NLS, whereas Candida albicans hyphae induce morphologically distinct NETs. By combination of quantitative data and image-based assessment, both structures can be discriminated from each other. In addition, we have established that during neutrophil and C. albicans interaction, citrullination of histone mainly stems from candidalysin. We show here and others have shown previously (10.3389/fimmu.2018.01573) that citrullination of histone occurs during but is not required for NET formation. But histone citrullination is promoted mainly by candidalysin and is also required for formation of NLS. Thus, histone citrullination constitutes another important discriminatory factor between NETs and NLS.

We added modified and added text to the respective figure legend: (line 188) ”To allow comparability, NLS were quantified with the same criteria as previously described for NETs. Data shown as mean ± SEM. Confocal images (c) of immunostained cells display morphological changes involving nuclear and granular proteins after 4 h compared to unstimulated cells or 100 nM PMA, or cells exposed to scrambled candidalysin and pep2. The morphological changes evoked by PMA considerably deviate from morphological changes evoked by candidalysin and, hence, are defined as NETs (for PMA) and NLS (for candidalysin).”

*10/ 190 allows a more detailed view of the neutrophil-derived structures (Error! Reference source not Please, eliminate this error. *

Response:

Thank you for pointing this out to us. We have fixed this error.

*11/ 193 Ionomycin has been previously reported to induce NLS, also... 194 Both, PMA and ionomycin generated widespread chromatin fibers in the extracellular space 197 In addition, C. albicans hyphae induced NETs with observable fibers and 198 threads similar to PMA- and ionomycin-stimulated neutrophils (Fig. 3b). 199 Image-based quantification of NLS events (candidalysin and ionomycin)

In a sentence earlier (193) you mentioned that the action of PMA leads to classical netosis and ionomycin leads to NLS. You pointed out earlier that NLS are poorly developed NETs (line 100), and here you write that PMA and ionomycin generate the same developed structures. You again differentiate between these structures depending on the stimulating factors. Pointing out the differences between the two forms, you should be more precise and consistent in your descriptions. This comment applies to the entire manuscript. *

Responses:

Thank you, we agree that consistency and clarity is required to describe the observed phenomena. We therefore modified or included the following sentences to the manuscript:

• (line 203) ”PMA exposure generated widespread chromatin fibres in the extracellular space (Fig. 3a, left panels) whereas ionomycin exposure resulted in more compact, patchy areas occasionally dispersed with long, thin chromatin fibres (Fig. 3b, middle panels). With regard to morphological changes, candidalysin treatment resulted in compact, fibrous structures resembling those stemming from ionomycin treatment, however long, thread-like structures were absent in candidalysin-treated neutrophil samples (Fig. 3a right panels, for 7 h treatment see Fig. S1c)”
• (Line 513) ”While ionomycin- and candidalysin-induced NLS shared similar key features, such as increased histone citrullination, our study revealed striking differences between the two toxins. In contrast to ionomycin, candidalysin stimulation led to ROS production in neutrophils.”

  12/ 203 NLS after 3 h and 5 h, respectively, and led to overall fewer NLS events. This was confirmed by observation. 204 area-based analysis of the events (Fig. 3d). The average area per event that exceeded 100 μ*m2 was 205 determined using the images from the DNA stain. What is the accepted criterion for distinguishing between NLS and NETs? *

Response:

The main criteria distinguishing canonical NETs from NLS is a higher compactness for NLS and an increased citrullination of histones, the latter being absent in canonical NETs (10.3389/fimmu.2016.00461; 10.1016/j.mib.2020.09.011). Please see our comment above (regarding reviewer comment 9). Comparing candidalysin and ionomycin as stimuli for NLS they share key similarities, such as increased citrullination of histone (Fig. 3) and more compact structures than NETs (Fig. 3) with an average size of 151 µm2 for candidalysin-induced and 149 µm2 for ionomycin-induced NLS compared to 262 µm2 for PMA-induced and 231 µm2 for C. albicans-induced NETs (for clarification these average sizes are stated in the text). However, the NLS triggered by candidalysin and ionomycin also show differences. Ionomycin occasionally results in extended chromatin threads, whereas candidalysin does not. Ionomycin induces no ROS at all, whereas candidalysin does to some extent. By consistent usage of the definitions for NETs and NLS and by pinpointing the differences between ionomycin and candidalysin in terms of NLS induction (which are previously unknown) we hope we have sufficiently addressed this comment.

*13/ line 218, 243 - reference error *

Response:

Thank you, we have fixed this error

14/ What form are we actually talking about? Are we focusing on the effect of a natural agent or a synthetic one in relation to NLS/NET? Perhaps it is more important to focus on the citrullination process.

• 247 synthetic candidalysin only induces NLS, we concluded that candidalysin augments NET release when the toxin is secreted by C. albicans hyphae. 256 This confirmed that candidalysin promotes C. albicans-triggered NET release. 262 Interestingly, the addition of synthetic candidalysin resulted in a shift to NLS, 274 External addition of synthetic candidalysin resulted in a shift to NLS structures rather than NETs as visualized by microscopy after 5 h incubation (20X).*

Response:

We used the adjective “synthetic” here to make clear that this is a synthetized peptide and not candidalysin isolated from growing C. albicans. Having said that, we fully agree that the synthetized peptide and the one released by C. albicans cells are essentially identical on the molecular level and thus it is irrelevant and confusing to state in this context here. Therefore, we removed the adjective “synthetic” throughout the study and refer the reader to the method section for information on the origin of candidalysin used in the study. At times, we state “candidalysin alone” when we want to emphasize that candidalysin was the sole trigger used for the respective assay.

15/ Has there been any method to track candidalysin production during contact of C. albicans with neutrophils?

Responses:

Thank you for this comment. Yes, there is a QVQ nanobody that can be used which is currently not to our disposal (doi.org/10.1111/cmi.13378). However, we already know from this publication that candidalysin concentrations vary when released naturally. The concentrations are particularly high in invasion pockets or dense biofilms. We also know that if we add candidalysin to the medium we have even distribution throughout and this is by definition different from concertation spikes at host cell-fungal interaction sites. As we have stated above, hyphal tips in turn are readily attacked by human neutrophils (doi.org/10.1189/jlb.0213063). Hence, we can safely assume, according to these previous publications, that there will be a more uneven distribution of candidalysin concentrations over neutrophil membranes, when the sole source of the toxin stems from growing hyphae interacting with neutrophils. It would of course be very interesting to know how the toxin exactly intercalates into membranes and which morphologies potential pores may have. These questions are currently under investigation in the laboratories of B. Hube and J. Naglik. To incorporate these findings here would certainly be far beyond the scope of this study.

We include and modify the following sentences to the discussion of this manuscript to clarify the issue: (Line 544). ” Lack of candidalysin production in C. albicans results in significantly reduced histone citrullination, accompanied with decreased NET formation. However, citrullination is not required for NET release, but rather governs the formation of NLS, which is dominant when candidalysin is added exogenously with even distribution throughout the cell suspension. With regard to C. albicans hyphae secreting candidalysin, local concentrations of the toxin are likely to vary to a large degree, particularly when the candidalysin-secreting hypha is engulfed by a neutrophil. Therefore, it may be difficult to discriminate NLS form NETs during the interaction of neutrophils and C. albicans, as both structures may be induced concurrently 10. It seems logical that the pore-forming activity of candidalysin augments the release of NET fibres during C. albicans infection, where PRRs will additionally be triggered on neutrophils, resulting in combinatorial activation of downstream pathways. In line with this notion, candidalysin drives histone citrullination, which contributes to chromatin decondensation.”

*16/ In Figure 4f-the given information indicates 1,2 hour incubation, in the caption of the figure there is information about 5 hour incubation - please clarify. The description of the stains used is lacking. *

Response:

Microscopic analysis performed after 5h incubation time, whereas candidalysin has been added to different time points indicated in the Figure (in the new version this is now Figure 8f). We clarified in the legend as follows: (line 472) “(f) Neutrophils were infected with C. albicans and 15 µM candidalysin was added 0 h, 1 h or 2 h after the infection. Addition of candidalysin at the different time points after C. albicans infection resulted in a shift to NLS structures rather than NETs as visualized by microscopy after 5 h total incubation (20X).” The description of the strains is depicted directly in the Figure, next to the microscopic images.

*17/ Fig. 5 - result for 15 uM MitoTEMPO - adds nothing to the results and introduces image information noise - should be removed. No information on the concentration of the peptide used. *

Responses:

We would like to keep the 15 µM MitoTEMPO concentration, since it is the more reasonable concentration at which we do not observe an effect. This argues that ROS is more-likely derived from NADPH oxidase and not mitochondrial ROS. We show TEMPOL effects at 15 µM and at 100 µM to document the dose dependency and for the sake of comparability, we would like to keep both concentrations also for MitoTEMPO.

The indicated peptide concentration was added to the figure legend. Thank you for pointing this out.

*18 / Fig. 5, line 309: and cell-permeable Sytox Green DNA dye (250310 nM) to determine the total number of cells".

Please correct the information on the use of both dyes, according to the manufacturer's description: "SYTOX® Green nucleic acid stain is an excellent green-fluorescent nuclear and chromosome counterstain that is impermeant to live cells, making it a useful indicator of dead cells within a population." *

Response:

Thank you for highlighting this error. Indeed, we used Syto Green for this particular staining, a dye which stains both live and dead cells since the dye is cell-permeable. We corrected the error at this section of the text.

*19/ 324 At later time points, BAPTA-AM led to an increase in NLS, probably due to toxic effects as indicated by higher background levels of NLS formation in non-stimulated, BAPTA-AM-treated neutrophils (Fig. 6d).

If such an assumption is made, the toxic effect should also be observed for the control. *

Response:

The toxic effect was observed while conducting the experiments, but cannot be seen in the size-base quantification which is the read out for this particular experiment. We have performed a cytotoxicity assay using flow cytometry and PI staining to confirm the effect. The results are added as supplemental Figure (Fig. S3b).

*20/Fig. 6C PAD inhibitor should affect PMA-induced netosis, but the figure presents NLS existence - how was this change found? *

Responses:

We are grateful for the opportunity to explain this more thoroughly. PMA does not trigger histone citrullination (10.3389/fimmu.2016.00461) and thereby there is no effect of the PAD inhibitor on PMA-induced NETs. Notably, some level of histone citrullination can also be observed in unstimulated neutrophils (see Fig. 3, 5 and 8), since histone modification is not exclusively dependent on stimulation. However, upon PMA stimulation we observe a decrease (Fig. S1b), not an increase, of histone citrullination consistent with previous reports.

We adjusted the text as follows: (line 235) “. Expectedly, citH3 levels upon PMA stimulation did not increase, but rather decreased which is consistent with previous reports 10 (Fig. 3d and Suppl. Fig. S1b). While citrullination levels in unstimulated neutrophils decreased over time, ionomycin stimulation sustained high levels over 5 h.

*21/ line320 "This indicates that candidalysin most probably causes Ca2+ influx via pore formation and not via direct receptor stimulation" And: line 358. As C.albicans hyphae bind to pathogen recognition receptors (PRRs), activate neutrophils and ultimately promote the release of NETs, we aimed to elucidate whether candidalysin alone leads to the activation of similar pathways in neutrophils. Hence, we stimulated neutrophils with candidalysin in the presence or absence of specific inhibitors for SYK, PI3K, and Akt.

Lack of consistency in conclusion. *

Response:

Thank you for pointing this out. We adjusted the paragraph (line 331) as follows: “As C. albicans hyphae bind to pathogen recognition receptors (PRRs), activate neutrophils and ultimately promote the release of NETs, we aimed to elucidate whether candidalysin alone can trigger similar pathways in neutrophils via signalling cross talk induced by Ca2+ influx. Hence, we stimulated neutrophils with candidalysin in the presence or absence of specific inhibitors for SYK, PI3K, and Akt (Fig. 6b).”

*22/ Fig. 7 It would be good to verify these results with experiments using mutants. Figures 7b, 7c, and 7d can be combined to make the whole drawing clearer. *

Response:

We thought this is very relevant and included additional experiments showing that the mutant strains also induce phosphorylation of lamin A/C independent of the expression of candidalysin (new Fig. 6e and 6f).

*23/ line 603 'The percentage of dead cells was calculated using TritonX-100 lysed neutrophils as 100% control' - maybe use " treated or permeabilized" *

Response:

Thank you, we changed the phrasing accordingly.

Reviewer #1 (Public Review):

The authors aimed to contrast the effects of pharmacologically enhanced catecholamine and acetylcholine levels versus the effects of voluntary spatial attention on decision making in a standard spatial cueing paradigm. Meticulously reported, the authors show that atomoxetine, a norepinephrine reuptake inhibitor, and cue validity both enhance model-based evidence accumulation rate, but have several distinct effects on EEG signatures of pre-stimulus cortical excitability, evoked sensory EEG potentials and perceptual evidence accumulation. The results are based on a reasonable sample size (N=28) and state-of-the art modeling and EEG methods.

Although the authors draw a few partial conclusions that are not fully supported by the data (see below), I think that the authors' EEG findings provide sufficient support for the overall conclusion that "selective attention and neuromodulatory systems shape perception largely independently and in qualitatively different ways". This is an important conclusion because neuromodulatory systems and selective spatial attention are both known to regulate the neural gain of task-relevant single neurons and neural networks. Apparently, these effects on neural gain affect decision making in dissociable ways.

The effects of donepezil, a cholinesterase inhibitor, were generally less strong than those of atomoxetine, and in various analyses went in the opposite direction. The authors fairly conclude that more work is necessary to determine the effects of cholinergic neuromodulation on perceptual decision making.

1) I believe that the following partial conclusions are not fully supported by the data:

a) 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".

b) "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)."<br /> 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.

c) 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)."<br /> 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.

2) 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.

I think that this is true. We are so busy with creating things that are technologically advanced and never thinking about whether or not the invention is good and if this invention may lead to something negative. For example, ChatGPT has been viewed with many different opinions, it can be very helpful to us, but in some ways or in further applications, it may actually be really harmful to us.

• "gestation rewires your brain in fundamental ways um you it rewire it primes you for caretaking as a as a mother in a way which is far more visceral and far it's it's pre-rational it's it's immensely transformative experience and it's permanent you know once you've been rewired for mummy brain you'd never really go back um and that from the point of view of raising a child that matters um because when after a baby is born it's you know as winnicott once said you know there's no such thing as a baby there's only a baby and someone there's a a baby doesn't exist as an independent entity until it's some years some years into its life arguably quite a few years into its life um and what I would say about artificial wounds is that you may be you may think that what you're doing is creating a baby without the misery of gestation but what you're doing in practice is creating a baby without creating a mother because a pregnancy doesn't just create a baby it also creates a mother"

• Comment

  • This is alluding to our altricial nature, which makes us human INTERbeings from before birth
  • https://jonudell.info/h/facet/?max=100&expanded=true&user=stopresetgo&exactTagSearch=true&tag=altricial
  • We are socially entangled even before our birth

• comment
  • I think many of us have had this thought!
    • that when we die, vast amounts of wisdom is extinguished along with that person
    • As our digital tools become more sophisticated, however,
  • we are uploading our libraries to the digital collective intelligence network
    • the internet may well evolve to become the epitome and master repository of human cumulative cultural evolution.
    • even AI could not exist if it did not mine a training set of billions of human and their shared ideas
    • Perhaps it is the internet which is the vehicle for collective hybridized human-cyborg immortality?
    • If knowledge is preserved this way, then this flavor of immortality is only meaningful for our species

Reply to Nick at https://forum.zettelkasten.de/discussion/comment/17926/#Comment_17926

Some pieces of social media come close to the sort of sense making and cognition you're talking about, but none does it in a pointed or necessarily collaborative way. The Hypothes.is social annotation tool comes about as close to it as I've seen or experienced beyond Wikipedia and variations which are usually a much slower boil process. As an example of Hypothes.is, here's a link to some public notes I've been taking on the "zettekasten output problem" which I made a call for examples for a while back. The comments on the call for examples post have some rich fodder some may appreciate. Some of the best examples there include videos by Victor Margolin, Ryan Holiday (Robert Greene's protoge), and Dustin Lance Black along with a few other useful examples that are primarily text-based and require some work to "see".

For those interested, I've collected a handful of fascinating examples of published note collections, published zettelkasten, and some digitized examples (that go beyond just Luhmann) which one can view and read to look into others' practices, but it takes some serious and painstaking work. Note taking archaeology could be an intriguing field.

Dan Allosso's Obsidian book club has kept up with additional books (they're just finishing Rayworth's Doughnut Economics and about to start Simon Winchester's new book Knowing What We Know, which just came out this month.) Their group Obsidian vault isn't as dense as it was when they started out, but it's still an intriguing shared space. For those interested in ZK and knowledge development, this upcoming Winchester book looks pretty promising. I'd invite everyone to join if they'd like to.

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Reply to the reviewers

1. General Statements

We would like to thank the reviewers for their professional comments and constructive suggestions. Our current plan is to revise the manuscript and supplemental materials in response to the reviewers’ requests and suggestions. Toward this goal we began experiments to obtain new data requested by the reviewers and anticipate the outlined experiments can be completed within the next three months.

2. Description of the planned revisions:

__Reviewer #1: __

The results of experiments where Arp2/3 is blocked (Fig.2) should be confirmed by Arp2/3 knock-down and with an independent Arp2/3 inhibitor. Several are available (CK-869, Benproperine, Pimozide). For Fig.3 and 4, that would not be necessary, but to establish the specificity of the effect in fig.2 this is absolutely required.

__Response: __As requested, we will include new data with CK-869, the indicated Arp2/3 complex inhibitor. We purchased the inhibitor and are currently confirming its efficacy before testing whether it inhibits transition to the hESC naïve state. However, we respectfully disagree with generating a Arp2/3 knock-down hESC line. Arp2/3 complex genes are known to be essential genes in both mouse and human embryonic stem cells (PMID: 29662178 and PMID: 31649057). Furthermore, reports on successful knockout of complex subunits indicate that additional genetic manipulations are needed to maintain cell survival, including knockout of INK4A/ARF to bypass apoptosis associated with Arp2 shRNA knockdown (PMID: 22385962) and genetic manipulations in mouse models (PMID: 22492726. Thus, knock-down of Arp2/3 complex members in our cells is beyond the scope of this manuscript.

Yilmaz A, Peretz M, Aharony A, Sagi I, Benvenisty N. Defining essential genes for human pluripotent stem cells by CRISPR-Cas9 screening in haploid cells. Nat Cell Biol. 2018 May;20(5):610-619. doi: 10.1038/s41556-018-0088-1. Epub 2018 Apr 16. PMID: 29662178.

Shohat S, Shifman S. Genes essential for embryonic stem cells are associated with neurodevelopmental disorders. Genome Res. 2019 Nov;29(11):1910-1918. doi: 10.1101/gr.250019.119. Epub 2019 Oct 24. PMID: 31649057; PMCID: PMC6836742.

Wu C, Asokan SB, Berginski ME, Haynes EM, Sharpless NE, Griffith JD, Gomez SM, Bear JE. Arp2/3 is critical for lamellipodia and response to extracellular matrix cues but is dispensable for chemotaxis. Cell. 2012 Mar 2;148(5):973-87. doi: 10.1016/j.cell.2011.12.034. PMID: 22385962; PMCID: PMC3707508.

I believe that the status of the actin cytoskeleton in both states is not well enough characterized. This is especially obvious for branched actin networks themselves that depend on the Arp2/3. To this end, the authors may localize Arp2/3 or cortactin, a useful surrogate that often gives a better staining. This point is particularly important since contractile fibers are not made of branched actin. Myosin cannot walk or pull along branched actin networks because of steric hindrance. It might well be that branched actin networks are debranched after Arp2/3 polymerization. I suggest staining tropomyosins that would indicate where the transition between branched and unbranched actin would be. Along this line, phosphoERMs should be localized and revealed by Western blots (we expect an increase from primed to naive state) because they cannot perform the proposed function of linker between the membrane and actin filaments if they are not phosphorylated.

Response: As requested we will include new data with cortactin immunolabeling, which we already completed. These new data, shown below, confirm that cortactin, which binds to branched actin filaments, co-localizes with the F-actin fence around hESC naïve colonies, suggesting that the fence includes branched F-actin. Also as requested, we are currently immunoblotting for phosphorylated ERMs to more thoroughly assess if they may serve as a linker between the membrane and actin filaments.

Branched actin is required for cell cycle progression and cell proliferation in normal cells. This requirement is lost in most cancer cells (Wu et al., Cell 2012; Molinie et al., Cell Res 2019). This would be really important to know whether ESCs stop proliferating upon CK-666 treatment. In other words, do they behave like normal cells or transformed cells. Proliferation is a major function that depends on the YAP pathway. Cell counts and EdU incorporation can easily provide answers to this important question.

__Response: __As requested, we will include new data on proliferation. We anticipate that these new data will complement data we already have showing that CK-666 does not impair proliferation compared with hESC controls. We also note that the role of the actin cytoskeleton in proliferation is well established and an increase in proliferation is a hallmark of acquisition of the naïve state of pluripotency (PMID: 35005567).

Chen C, Zhang X, Wang Y, Chen X, Chen W, Dan S, She S, Hu W, Dai J, Hu J, Cao Q, Liu Q, Huang Y, Qin B, Kang B, Wang YJ. Translational and post-translational control of human naïve versus primed pluripotency. iScience. 2021 Dec 17;25(1):103645. doi: 10.1016/j.isci.2021.103645. PMID: 35005567; PMCID: PMC8718978.

Minor Comments:

What about the rescue of cell morphology? Does active YAP restore the intercellular contractile bundle?

__Response: __As requested, we obtained these data, as shown below. Expression of the YAP-S127A mutant does rescue the formation of the actin ring architecture in the presence of CK666. We are currently performing additional dedifferentiation assays to immunolabel for pMLC and address the question of if expression of YAP-S127A restores the contractile bundle.

__Reviewer #2: __

The authors found that a ring of actin filaments at the colony periphery was characteristic of the naive hESCs. However, because all the data are presented as an image of a single confocal section, the 3D organization of the actin filaments is not clear. Although the authors drew a scheme for this actin ring being located in the apical domain of polarized cells, such data have not been provided in the manuscript. Since naive hESCs form dome-like colonies, it is important to show the 3D organization of actin filaments in the colony. 3D reconstruction of confocal microscopy images of the naive hESC colonies is required to show the relationship between actin filaments, adherens junctions, and the nuclei (as a reference for the Z axis). If 3D reconstruction is not technically possible, confocal images at different Z levels and maximum projection images should be obtained and provided.

__Response: __As requested, we are currently generating 3D images of the actin fence by using Imaris software, which we previously used to show 3D images of mitochondrial morphology (PMID: 34038242)

Manoli SS, Kisor K, Webb BA, Barber DL. Ethyl isopropyl amiloride decreases oxidative phosphorylation and increases mitochondrial fusion in clonal untransformed and cancer cells. Am J Physiol Cell Physiol. 2021 Jul 1;321(1):C147-C157. doi: 10.1152/ajpcell.00001.2021. Epub 2021 May 26. PMID: 34038242; PMCID: PMC8321791.

Some of the statistical analyses were inappropriate. The authors have used Student's t-test for all analyses; however, one-way ANOVA and post-hoc analysis must be used to compare three or more groups (Figs. 2B, D, E, 3G, 4B, D, E).

__Response: __As requested, we will re-evaluate our statistical analysis. We note that our submission reports comparisons between two groups, and hence, Student’s t-test is appropriate. For example, we compared primed and naïve to demonstrate successful acquisition of naïve pluripotency, and then we compared the naïve condition to the CK666-treated conditions to demonstrate the impact of CK666-treatment. As Reviewer 2 suggests we will reanalyze all quantifications using one-way ANOVA with post-hoc analysis in the full revision and we will also discuss with Stuart Gansky, a statistician at UCSF whom we previously consulted for most appropriate statistical analysis of our studies.

Minor Comments:

Page 9, second paragraph. In the discussion section, authors have written that "Cells within the ICM of mouse blastocysts exclude YAP from the nucleus whereas cells within the ICM of human blastocysts maintain nuclear YAP." However, a recent study has reported that the ICM/epiblast of mouse late blastocysts also express nuclear YAP. Epiblast Formation by TEAD-YAP-Dependent Expression of Pluripotency Factors and Competitive Elimination of Unspecified Cells. Hashimoto M, Sasaki H. Dev Cell. 2019, 50:139-154.e5. doi: 10.1016/j.devcel.2019.05.024.

__Response: __As requested, we will revise our Discussion section to include findings from the indicated new publication.

Reviewer #3:

Many of their conclusions seem to be based on the qualitative analysis of a single image (e.g. Figures 1D-G, Fig 2G, Supplementary Figure 2). The authors should provide quantitative information regarding these analyses and indicate the number of cells/replicas collected for each experiment.

__Response: __As requested, our revision will have added quantitative data when feasible. We note that in the field, traction force microscopy isn’t commonly quantified beyond including scale bars, which our original manuscript shows. Moreover, pluripotency is standardly not quantified because it is a binary switch - cells are either double positive or they are not. We show 100% double positive, and rtPCR data with known stage-specific markers.

The actin ring surrounding hESCs colonies was previously described by Närvä et al. Although the authors cited this previous work, they do not discuss in deep the differences and similarities with their observations.

__Response: __As requested, our revised manuscript with include additional detail comparing our results with those from Närvä et al. In brief, we observe the formation of this actin ring only in the naïve state of pluripotency, whereas Närvä et al. observe an actin architecture in the primed state. One possible source of difference between their study and ours are the cells used for analysis. Närvä et al. utilize induced pluripotent stem cells, long since proposed to be closer to naïve pluripotency than primed stem cells as conventionally isolated and maintained (see PMID: 27424783 and PMID: 19497275). Additionally, we observe that the contractile actin ring in naïve pluripotent stem cells is in a higher z-plane than reported by Närvä et al., although a direct comparison is difficult to make.

Theunissen TW, Friedli M, He Y, Planet E, O'Neil RC, Markoulaki S, Pontis J, Wang H, Iouranova A, Imbeault M, Duc J, Cohen MA, Wert KJ, Castanon R, Zhang Z, Huang Y, Nery JR, Drotar J, Lungjangwa T, Trono D, Ecker JR, Jaenisch R. Molecular Criteria for Defining the Naive Human Pluripotent State. Cell Stem Cell. 2016 Oct 6;19(4):502-515. doi: 10.1016/j.stem.2016.06.011. Epub 2016 Jul 14. PMID: 27424783; PMCID: PMC5065525.

Nichols J, Smith A. Naive and primed pluripotent states. Cell Stem Cell. 2009 Jun 5;4(6):487-92. doi: 10.1016/j.stem.2009.05.015. PMID: 19497275.

The qualitative observation of Figure 3F suggests a lower overall YAP levels in primed and +CK666 cells in comparison to naive cells. Could the authors check if this is correct and, if this is the case, explain the observation?

__Response: __As requested, our revision will include new data on YAP protein expression by immunoblotting.

The authors should discuss deeper the rationale of the pan-ERM immunostaining experiments (since they used the individual antibodies afterwards) and provide a brief discussion of their results and, in particular, the colocalization with moesin but not with ezrin or radixin.

__Response: __As requested, our revised manuscript will include a more detailed discussion of our results with ERM immunolabeling.

2. Description of the revisions that have already been incorporated in the transferred manuscript:

__Reviewer #1: __

Minor Comments:

Fig2F: non-representative pictures or wrong quantification of the CK666 condition.

__Response: __We thank the review for alerting us to this error. The CK666 Primed and Naïve condition images were swapped. We have edited the figure to correct this.

Fig3A: Y-axis? What is it? How is it adjusted? -Log P?

__Response: __Please see the methods section. Differential expression analysis was performed using DESeq2 R package. The resulting P values were adjusted (padj) using the Benjamini and Hochberg’s approach for controlling the False Discovery Rate (FDR). Genes with a padj

Colors of dots not really visible (in reference to Figure 3A).

__Response: __We thank the reviewer for this comment and have updated the figure to use more standard, colorblind-friendly color choices (see the above figure). Additionally, we fixed a drawing error in the figures when creating the volcano plots.

Typos: Apr2/3 in the abstract, Hoeschst in Fig.S1B.

__Response: __We thank the review for alerting us to these errors. We have edited the manuscript to correct them.

__Reviewer #3: __

There are many experimental details missing that are extremely relevant to fully understand the experiments and evaluate the robustness of the analyses (e.g., microscopy setup, fluorescent probes used for immunostaining, incubation conditions with the inhibitors SMIFH2 and CK666).

__Response: __As requested we have updated the Materials and Methods section with more detailed information on procedures and reagents.

Minor Comments:

The Introduction makes the reader think that actin is the only cytoskeletal network involved in embryo development and stem cell properties. They should also include a brief discussion on the relevance of the other cytoskeletal networks in mechanotransduction and cell fate decisions.

__Response: __As requested, we will revise our Introduction. We note, however, that in the field additional cytoskeleton components, including intermediate filaments and microtubules have mostly been shown for interacting with the nucleus with limited evidence for roles in differentiation.

Many of the images seem to require a flat-field correction. Could the authors check that the illumination is homogeneous? This artifact could affect the data analysis.

__Response: __As we indicate in the Methods section, the spinning disc confocal microscopes used in our study are equipped with a Borealis to mitigate uneven illumination across the field of view. Additionally, quantification in Figures 2C-E, Figures 3F-G, and Figures 4A-D are comparing measurements to a local background (i.e. cytoplasm nearby) in order to normalize for any uneven illumination effects.

There are many abbreviations that are not defined in the text and are extremely specific to the field.

__Response: __As requested, we have expanded the definition of many abbreviations in the text and any additional abbreviations changes will be clearly defined in our revised manuscript.

Could the authors explain the selection of the pluripotency markers studied by qPCR? Specifically, why they studied DNMT3L, DPPA3, KLF2, and KLF4 (Fig. 1B) and the different set PECAM1, ESRRB, KLF4, and DNMT3L in Fig. 2B.

__Response: __Defining the exact molecular and cell behavioral characteristics of naïve pluripotency remains an evolving point of development within the field. The pluripotency markers used in both original panels are known and established markers of naïve pluripotency. The original panel of DNMT3L, DPPA3, KLF2, and KLF4 was established based upon RNAseq datasets publicly available, whereas the secondary panel of PECAM1, ESRRB, KLF4, and DNMT3L was a more targeted analysis of genes found in the literature which have been interrogated in more detail for potential roles in naïve pluripotency. To facilitate clarity within the manuscript, we have updated Fig. 1B to match Fig. 2B for the purposes of defining a transcriptional hallmark of naïve pluripotency for the purposes of this manuscript.

Figures 1G and 2G, please include the images of the colonies.

__Response: __As requested, our revised manuscript will include phase contrast images, which we already have, as shown below. These images will be included Supplemental Figure 1 and Supplemental Figure 2 for the colonies used to show representative tractions in Figure 1G and 2G, respectively.

3. Description of analyses that authors prefer not to carry out

Reviewer #1:

The results of experiments where Arp2/3 is blocked (Fig.2) should be confirmed by Arp2/3 knock-down and with an independent Arp2/3 inhibitor. Several are available (CK-869, Benproperine, Pimozide). For Fig.3 and 4, that would not be necessary, but to establish the specificity of the effect in fig.2 this is absolutely required.

__Response: __As requested, we will include new data with CK-869, the indicated Arp2/3 complex inhibitor. We purchased the inhibitor and are currently confirming its efficacy before testing whether it inhibits transition to the hESC naïve state. However, we respectfully disagree with generating a Arp2/3 knock-down hESC line. Arp2/3 complex genes are known to be essential genes in both mouse and human embryonic stem cells (PMID: 29662178 and PMID: 31649057). Furthermore, reports on successful knockout of complex subunits indicate that additional genetic manipulations are needed to maintain cell survival, including knockout of INK4A/ARF to bypass apoptosis associated with Arp2 shRNA knockdown (PMID: 22385962) and genetic manipulations in mouse models (PMID: 22492726. Thus, knock-down of Arp2/3 complex members in our cells is beyond the scope of this manuscript.

Yilmaz A, Peretz M, Aharony A, Sagi I, Benvenisty N. Defining essential genes for human pluripotent stem cells by CRISPR-Cas9 screening in haploid cells. Nat Cell Biol. 2018 May;20(5):610-619. doi: 10.1038/s41556-018-0088-1. Epub 2018 Apr 16. PMID: 29662178.

Shohat S, Shifman S. Genes essential for embryonic stem cells are associated with neurodevelopmental disorders. Genome Res. 2019 Nov;29(11):1910-1918. doi: 10.1101/gr.250019.119. Epub 2019 Oct 24. PMID: 31649057; PMCID: PMC6836742.

Wu C, Asokan SB, Berginski ME, Haynes EM, Sharpless NE, Griffith JD, Gomez SM, Bear JE. Arp2/3 is critical for lamellipodia and response to extracellular matrix cues but is dispensable for chemotaxis. Cell. 2012 Mar 2;148(5):973-87. doi: 10.1016/j.cell.2011.12.034. PMID: 22385962; PMCID: PMC3707508.

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Reply to the reviewers

1. General Statements

We thank the reviewers for their constructive feedback, which has helped us improve the manuscript considerably (no comment on whether the improvements are “significant”). Below are our point-by-point responses. We have also highlighted all changes in the manuscript.

2. Point-by-point description of the revisions

Reviewer 1

Summary

In this study, Obodo et al. present a new iteration of their popular rhythm analysis tool LimoRhyde. The conceptual advancement in this new iteration is the focus on effect sizes (in the form of point estimates of amplitude and their prediction intervals) rather than the p-values, which has been the predominant form of statistical testing for rhythm analysis. Therefore, compared to a well-established non-parametric method for rhythm testing, LimoRhyde2 selects genomic features with larger amplitudes (effect-sizes) as it is designed to do.

Major Comments

1. (LimoRhyde2 algorithm, Page 2-) It is unclear what exactly the contributions/advancements of the authors are? Is it a novel statistical method, the combination of well-established tools in a novel workflow, or is it a novel application to a new field (rhythms)? I am afraid the sentence "LimoRhyde2 builds on previous work by our group and others to rigorously analyze data from genomic experiments [9,16,17], capture non-sinusoidal rhythms [18], and accurately estimate effect sizes [14,19]." is rather ambiguous.

We have revised this sentence in the last paragraph of the Introduction to clarify LimoRhyde2’s contributions.

1. (Moderate model coefficients, Page 3-) The authors implement empirical Bayes shrinkage on the coefficients. But the state-of-the-art methods used in LimoRhyde2 for linear model fitting, such as DESeq2/limma-voom/limma-trend, already implement shrinkage for the coefficients. Does algorithm implement a second round of Bayes shrinkage on the rhythm effect-sizes? How or why is this a statistically valid procedure? If not, how does Limorhyde2 add to shrinkage already implemented in DESeq2/limma-voom/limma-trend? Please elaborate.

To our understanding, the two shrinkage procedures work at different levels and serve different purposes. Limma applies shrinkage on residual variances to account for any technical variation and to give a higher power to detect effects for data with smaller sample sizes within each condition; it does not shrink coefficients. In practice, limma’s shrinkage has little effect given the relatively large sample sizes of most circadian experiments. LimoRhyde2, on the other hand, uses mashr to apply shrinkage to the coefficients themselves to account for shared patterns of effects and variation across both features and conditions. We see no reason this approach is invalid, and in our conversations with Matthew Stephens, the author of ashr and mashr, he felt the same. We elaborate on each method’s contributions in the Discussion (paragraph 2).

1. I think the goal to move to effect-sizes which lead to more reproducible results and better biological significance is sound and highly appreciated. However, to make the community switch to a completely different way of viewing their genomic analysis requires more convincing examples(s)/use-cases on why they should abandon the old method that they are used to. Now, results section merely shows that this algorithm performs as designed (to find large amplitude rhythms).

We appreciate the comment and acknowledge that some readers may be particularly attached to p-values and our current analysis may not wholly convince them of the value of effect sizes. We believe the manuscript stands on its own, however, and are using LimoRhyde2 to guide experiments whose conclusions we hope to describe in future work. Nonetheless, we have revised the Discussion (paragraph 4) to clarify that some known relevant genes highly ranked by LimoRhyde2 were underappreciated by BooteJTK.

1. Related to point 3, others have previously proposed using amplitude (effect-size) thresholds in addition to the p-value cutoffs (Lück & Westermark, 2016, Pelikan et al, 2022), how would the results of Limorhyde2 compare in a fairer contrast where both p-value and amplitude thresholds are implemented? Does the proposed sound method outperform the two-step approach. The authors may perform this analysis on their chosen datasets as well.

Thank you for raising this point. Indeed, one way to view LimoRhyde2 is as a data-driven balancing of raw effect size and p-value. However, the approach of considering both raw amplitude and p-value is uncommon and requires yet another arbitrary cutoff, which complicates any genewise ranking and side-by-side comparison with other methods. Thus, we have decided to not perform this analysis, and instead mention what we see as the advantage of LimoRhyde2 in the Discussion (paragraph 2).

1. I am also not completely convinced of the author's approach to compare their tool against BooteJTK. P-values only show ordering when the alternative hypothesis is true. P-values under the null hypothesis are uniformly distributed in [0,1] so would be meaningless for the purpose of ordering. Without knowing the ground-truth, ordering by p-values is rather risky. I understand the authors' difficulty. But maybe point 4 above yields a better evaluation strategy for LimoRhyde2.

If one accepts that these datasets have a non-zero number of “true” rhythmic genes, which to us seems more than reasonable, then we don’t see this is a large issue. Ranking by (adjusted) p-value is also the standard in differential expression analyses.

1. (OPTIONAL) LimoRhyde2 orders results by the point estimates of the effect-sizes (amplitudes). Is this biologically the most meaningful? Should the effect-size CIs be ordered at all? Maybe we only care about whether the lower limit of the CI is greater than a chosen threshold without any ordering. A discussion of this would be valuable to a user.

We discussed this issue amongst ourselves as well, and ultimately elected for simplicity in ranking by only the point estimate and not the credible interval. We have now mentioned this issue in the penultimate paragraph of the Discussion.

1. (OPTIONAL) If indeed the authors want to move away from p-values, one could argue that most of the insights from p-value analysis are or could be biased. So why compare against ordering by p-values at all in the results?

We are not arguing that results from p-value-based analyses are biased. We seek to show the differences on real data between an analysis based on p-values, the dominant approach in the field, and one based on estimated effect sizes. We believe this has greater potential to promote thoughtful progress than does outright rejection of p-values based on a purely theoretical argument.

Minor Comments

1. In page 3, it is unclear why averaging the three fits is the best thing to do? How bad would the performance be if m = 1 was chosen compared to m=3.

We have elaborated the relevant section of the Methods. For most genes in most datasets, the difference between m=1 and m=3 wasn’t much. However, m=1 tended to go noticeably sideways for some of the most rhythmic genes, depending on the relative locations of timepoints and spline knots, whereas m=3 did not.

1. In page 4, "To account for this uncertainty, LimoRhyde2 constructs..." was difficult to understand and sounded arbitrary. Please explain further.

We have revised this sentence.

1. Lachmann et al. (2021) also use bootstrap confidence intervals rather than p-values to quantify rhythmicity that ought to be mentioned.

We have now cited this paper in the Introduction.

Significance Comments

1. General assessment: The authors present an exciting new way of viewing results of high-throughput data analysis in the context of biological rhythms using a Bayesian-like approach. Previously work has revealed the flaws in focusing on p-values and how focusing of effect-sizes (in this context amplitudes) can yield more robust, reproducible results. Although this promises to also yield more biological meaningful results, it is unclear from this study how this might be.

See reply to Major Comment 3 above.

1. Advance: This study presents the first tool in the context of the rhythm analysis to provide prediction intervals for different rhythm parameters to facilitate a move away from the hypothesis testing framework of p-values. This is a technical advance in the field of rhythm analysis, but it is unclear what insights this could yield.

See reply to Major Comment 6 above.

Reviewer 2

Major Comments

1. The manuscript introduces a new tool to select rhythmic genes and to quantify amplitudes and phases. The authors combine splines, linear regression, Bayes sampling, and Mash. They focus on amplitudes instead p-values as in other packages. The performance and independence of JTK methods are illustrated using selected circadian expression profiles from different mammalian tissues. The paper is clearly written and provides a valuable extension of existing tools. I miss, however, an intuitive explanation of Mash.

Thank you.

1. I agree with their claim that amplitudes are quite important for physiological regulations. However, p-values are also helpful to explore, e.g., transcription factor binding sites. Moreover, amplitudes are taken into account in many studies (see e.g. papers of Naef, Korencic, Westermark, Ananthasubramaniam...). Since JTK or RAIN are non-parametric methods amplitudes are not in focus. The authors should discuss the biological relevance of amplitudes more clearly.

Thanks for raising this point. We are careful to limit our claims to bulk transcriptome data, and have tried to cite the relevant prior work. We have revised the Discussion to clarify what we see as the potential value of amplitudes, as illustrated by our analysis.

1. The selection of the 3 data sets and of specific genes seems reasonable since a range of technologies (microarrays versus RNS-seq), of durations (1 day versus 2 days), and of gene amplitudes are represented. Still the authors should comments their selections of data sets and genes.

We have added justification for our choices.

1. I find also the tissue-dependent phase distributions of clock-controlled genes of interest. However, a comparison with other studies (Zhang, GTEx from Talamanca et al.) and a discussion how amplitude thresholds such as 10%, 25%, 50% affect the phase distributions would be valuable.

Thank you for the suggestion. We initially explored several values of the amplitude threshold for those histograms (Figure S4C) before selecting the top 25%, all led to the same conclusion. We consider this a minor issue and tangential to the main point of the paper, so we have left the figure as is. We invite any interested reader to explore the publicly available results.

Reviewer 3

Summary

The authors developed LimoRhyde2, a method for quantifying rhythmicity in genomic data, and applied it to mouse transcriptome data from liver, lung, and suprachiasmatic nucleus (SCN) tissues. The method uses periodic spline-based linear models and an Empirical Bayes procedure (Mash) to produce posterior fits and rhythm statistics. LimoRhyde2 prioritizes high-amplitude rhythms of various shapes rather than monotonic rhythms with high signal-to-noise ratios, which contrasts with previous methods like BooteJTK. The authors demonstrated the value of LimoRhyde2 in quantifying rhythmicity and highlighted some of its advantages over traditional methods. However, they also acknowledged limitations, such as the inability to compare rhythmicity between conditions and the assumption of fixed rhythms.

Major Comments

1. The key conclusions are convincing, as the authors demonstrated LimoRhyde2's ability to fit non-sinusoidal rhythms and prioritize high-amplitude rhythms over monotonic rhythms with high signal-to-noise ratios. This is shown by the comparison with BooteJTK, a popular method in the field, and by the analysis of real circadian transcriptome data from mouse tissues. However, the authors acknowledged some limitations that could impact the method's broader applicability.

Thank you.

1. Data and methods are presented in a reproducible manner, with detailed descriptions of the periodic spline-based linear models, the use of Mash for moderating raw fits, and the calculation of rhythm statistics. This information is sufficient for other researchers to replicate the study and apply the LimoRhyde2 method to their own datasets. The code is available already.

Thank you.

1. Adequate replication and statistical analysis are provided, with the authors analyzing the same datasets using both LimoRhyde2 and BooteJTK to compare their performance. The use of Spearman correlation to assess the relationship between the adjusted p-values from BooteJTK and the amplitudes from LimoRhyde2 further supports the statistical rigor of the study.

Thank you.

Minor Comments

1. Addressing LimoRhyde2's limitations would help improve the study.

We have extensively addressed the method’s limitations to the best of our knowledge in Discussion paragraphs 6 and 7.

1. Authors could provide more details on how LimoRhyde2 could be applied to single-cell RNA-seq data to improve the presentation. Single-cell quantification over time would be a challenging task, so some insight into this would be appreciated, rather than a brief comment at the end of the paper.

Thank you for your interest in this topic. To do it justice, however, requires its own project and paper, so scRNA-seq is beyond the scope of the current paper.

Significance Comments

1. This study represents a technical advance in the field of genomic analysis of biological rhythms by introducing LimoRhyde2, a method that prioritizes high-amplitude rhythms and directly estimates biological rhythms and their uncertainty. The method's ability to capture non-monotonic rhythms and account for uncertainty makes it a valuable tool for researchers interested in understanding circadian systems and their physiological impact.

1. The work is placed in the context of existing literature, as the authors compare LimoRhyde2 with BooteJTK, a refinement of the popular JTK_CYCLE method. The comparison highlights the differences in output, prioritization, and runtime, demonstrating LimoRhyde2's potential advantages over traditional methods in the field.

2. However, BooteJTK is relatively underused compared to many other methods, partly because of the difficulty and time required to run the analysis. The paper would be improved by comparing LimoRhyde2 to JTK_Cycle itself, as well as RAIN and ARSER. The latter are the most commonly used methods for rhythm detection, and thus the value of the paper's findings would be far greater by comparing to these methods. Like LimoRhyde2, they are also not resource-intensive to run.

Thanks for your feedback on this point, which is one we discussed at length amongst ourselves. In the end, we decided on BooteJTK because it seems to be the best performing version of the most common method. ARSER and RAIN are simply not the standard, and based on our interpretation of the evidence, not generally superior to JTK. If we had selected the vanilla JTK_Cycle, we felt a reviewer could discard our results by saying "well, they're comparing their method to a version of a method known to be flawed". Given our objective to highlight the differences between prioritization based on estimated effect size and prioritization based on p-value, we do not see the value of including additional methods in the analysis.

1. LimoRhyde2's ability to efficiently prioritize large effects with functional significance in the circadian system can provide valuable insights for these researchers and advance the understanding of biological rhythms. The LimoRhyde2 approach is different to conventional reliance on arbitrary p- or q-values, which are taken as almost sacrosanct in the field as a measure of a dataset's worth. LimoRhyde2 could thus help to change this false perception of how to rate a circadian rhythm, which has particularly been ushered in by a reliance on JTK_Cycle p- and q-values as the method of choice for assigning meaningfulness to rhythms. Unfortunately, JTK_Cycle is very conservative and is limited to detecting sinusoidal-type rhythms. LimoRhyde2 could overcome these limitations (as RAIN does too) if widely adopted. However, to do this, it must be compared to things like JTK_Cycle directly.

See reply to Significance Comment 3 above.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In this study, Obodo et al. present a new iteration of their popular rhythm analysis tool LimoRhyde. The conceptual advancement in this new iteration is the focus on effect sizes (in the form of point estimates of amplitude and their prediction intervals) rather than the p-values, which has been the predominant form of statistical testing for rhythm analysis. Therefore, compared to a well-established non-parametric method for rhythm testing, LimoRhyde2 selects genomic features with larger amplitudes (effect-sizes) as it is designed to do.

Major Comments:

1. (LimoRhyde2 algorithm, Page 2-) It is unclear what exactly the contributions/advancements of the authors are? Is it a novel statistical method, the combination of well-established tools in a novel workflow, or is it a novel application to a new field (rhythms)? I am afraid the sentence "LimoRhyde2 builds on previous work by our group and others to rigorously analyze data from genomic experiments [9,16,17], capture non-sinusoidal rhythms [18], and accurately estimate effect sizes [14,19]." is rather ambiguous.
2. (Moderate model coefficients, Page 3-) The authors implement empirical Bayes shrinkage on the coefficients. But the state-of-the-art methods used in LimoRhyde2 for linear model fitting, such as DESeq2/limma-voom/limma-trend, already implement shrinkage for the coefficients. Does algorithm implement a second round of Bayes shrinkage on the rhythm effect-sizes? How or why is this a statistically valid procedure? If not, how does Limorhyde2 add to shrinkage already implemented in DESeq2/limma-voom/limma-trend? Please elaborate.
3. I think the goal to move to effect-sizes which lead to more reproducible results and better biological significance is sound and highly appreciated. However, to make the community switch to a completely different way of viewing their genomic analysis requires more convincing examples(s)/use-cases on why they should abandon the old method that they are used to. Now, results section merely shows that this algorithm performs as designed (to find large amplitude rhythms).
4. Related to point 3, others have previously proposed using amplitude (effect-size) thresholds in addition to the p-value cutoffs (Lück & Westermark, 2016, Pelikan et al, 2022), how would the results of Limorhyde2 compare in a fairer contrast where both p-value and amplitude thresholds are implemented? Does the proposed sound method outperform the two-step approach. The authors may perform this analysis on their chosen datasets as well.
5. I am also not completely convinced of the author's approach to compare their tool against BooteJTK. P-values only show ordering when the alternative hypothesis is true. P-values under the null hypothesis are uniformly distributed in [0,1] so would be meaningless for the purpose of ordering. Without knowing the ground-truth, ordering by p-values is rather risky. I understand the authors' difficulty. But maybe point 4 above yields a better evaluation strategy for LimoRhyde2.
6. (OPTIONAL) LimoRhyde2 orders results by the point estimates of the effect-sizes (amplitudes). Is this biologically the most meaningful? Should the effect-size CIs be ordered at all? Maybe we only care about what whether the lower limit of the CI is greater than a chosen threshold without any ordering. A discussion of this would be valuable to a user.
7. (OPTIONAL) If indeed the authors want to move away from p-values, one could argue that most of the insights from p-value analysis are or could be biased. So why compare against ordering by p-values at all in the results?

Minor Comments:

1. In page 3, it is unclear why averaging the three fits is the best thing to do? How bad would the performance be if m = 1 was chosen compared to m=3.
2. In page 4, "To account for this uncertainty, LimoRhyde2 constructs..." was difficult to understand and sounded arbitrary. Please explain further.
3. Lachmann et al. (2021) also use bootstrap confidence intervals rather than p-values to quantify rhythmicity that ought to be mentioned.

Significance

General assessment:

The authors present an exciting new way of viewing results of high-throughput data analysis in the context of biological rhythms using a Bayesian-like approach. Previously work has revealed the flaws in focusing on p-values and how focusing of effect-sizes (in this context amplitudes) can yield more robust, reproducible results. Although this promises to also yield more biological meaningful results, it is unclear from this study how this might be.

Advance:

This study presents the first tool in the context of the rhythm analysis to provide prediction intervals for different rhythm parameters to facilitate a move away from the hypothesis testing framework of p-values. This is a technical advance in the field of rhythm analysis, but it is unclear what insights this could yield.

Audience:

This will be useful to all chronobiologists (clinical and basic research) who use high-throughput genomic assays. Since this is an open R-package, I suspect most of those who want to will be able to easily use it. My expertise is in chronobiology, data science and systems biology.

Author Response

Reviewer #2 (Public Review):

The paper by Arribas et al. examines the coding properties of adult-born granule cells in the hippocampus at both single cell and network level. To address this question, the authors combine electrophysiology and modeling. The main findings are:

Noisy stimulus patterns produce unreliable spiking in adult-born granule cells, but more reliable responses in mature granule cells.

Analysis of spike patterns with a spike response model (SRM) demonstrates that adult-born and mature GCs show different coding properties.

Whereas mature GCs are better decoders on the single cell level, heterogeneous networks comprised of both mature and adult-born cells are better encoders at the network level.

Based on these results, the authors conclude that granule cell heterogeneity confers enhanced encoding capabilities to the dentate gyrus network.

Although the manuscript contains interesting ideas and initial data, several major points need to be addressed.

Major points:

1) The authors use and noisy stimulation paradigm to activate granule cells at a relatively high frequency. However, in the intact network in vivo, granule cells fire much more sparsely. Furthermore, granule cells often fire in bursts. How these properties affect the coding properties of granule cells proposed in the present paper remains unclear. At the very least, this point needs to be better discussed.

In vivo whole cell recordings of granule cells are very scarce. In our study, we based the design of our stimulus on recordings from the intact network in vivo (PerniaAndrade and Jonas 2014), which show that granule cells receive a wide range of frequencies, with a power spectrum that exhibits a power law decay. These properties are built in our noisy stimuli. These in vivo recordings have also reported the presence of theta oscillations, showing a peak in the spectrum. However, in our approach we deliberately removed these oscillations from our stimuli because it is best to fit GLMs using white noise or noise with an exponentially decaying autocorrelation (Paninski et al. 2004).

Thus, our choice of the stimuli is far from arbitrary, but rooted on experimental evidence from intact network in vivo recordings, together with previous knowledge about GLM/SRM fitting. This comment reveals to us that we did not clarify this enough in the manuscript. We are grateful to the reviewer for revealing this omission, since this is in fact an important aspect of the study strategy. In the revised manuscript, we brought these points up front in the results section when we introduce the stimulus for the first time, and more thoroughly discussed it in the Methods section that describes the stimulus.

Still, the bursts observed in granule cells are an important feature and they have been observed to be phase locked to the theta-gamma oscillations in vivo (Pernia-Andrade and Jonas 2014). In the revised version of the manuscript we included new experiments and simulations with stimuli that include a peak in theta frequency. We found that immature neurons also improve decoding performance with these theta modulated stimuli.

2) The authors induce spiking in granule cells by injection of current waveforms. However, in the intact network, neurons are activated by synaptic conductances. As current and conductance have been shown to affect spike output differently, controls with conductance stimuli need to be provided. Dynamic clamp is not a miracle anymore these days.

The use of dynamic clamp sounds in principle like a good suggestion. However, in the manuscript we have taken a different approach to enable the use of a single neuron GLM that uses currents as inputs. To control for the differences between mature and immature neurons we used currents with amplitude normalized by the input resistance, and both types of neurons were measured with the same technique to allow for the comparison.

Importantly, the GLM type model that we use assumes that the membrane potential is a linear convolution of the input, which permits a straightforward and robust fitting approach. We argue that this is not a minor issue, since using dynamic clamp would require a drastic modification of the model. Furthermore, the use of conductance stimuli would not allow for the straightforward model fitting we perform with our approach. The key point here is that the membrane potential would not be correctly approximated as a linear function of the conductance stimulus, precluding the fitting strategy.

Finally, at the moment we do not have the equipment to perform the suggested experiment, so this suggestion would require a big amount of time to acquire the equipment and set up the experiments in mature and immature neurons. In addition, we would have to change the model and develop a different fitting strategy. With the controls that we already have in the manuscript, we do not think dynamic clamp experiments would fundamentally change the conclusions of the manuscript. Thus, we argue that this is beyond a reasonable timeframe for this revision, but could be something to further explore in future. We now mention this possibility in the discussion.

3) The greedy procedure is a good idea, but there are several issues with its implementation. First, it is unclear how the results depend on the starting value. What we end up with the same mixed network if we would start with adult-born cells? Second, the size of the greedy network is very small. It is unclear whether the main conclusion holds in larger networks, up to the level of biological network size (1 million). Finally, the fraction of adult-born granule cells in the optimal network comes out very large. This is different from the biological network, where clearly four or five-week-old granule cells cannot represent the majority. Much more work is needed to address these issues.

The reviewer approves the greedy procedure that we apply in our manuscript and poses three issues for consideration.

First, the reviewer queries what would be the result of starting the procedure with a different pool of simulated neurons, and whether we would obtain “the same mixed network if we would start with adult-born cells”. Let us remark that the outcome of the greedy procedure is not always the same mixed population of neurons. For each different mature neuron that we use to start the procedure, the trajectory (see Fig. 4A) of selected neurons will be different. Thus, the final population (network) will be different, and this is reflected in the error bars that we obtain in Fig. 4. Presumably, starting with adult-born cells will change the outcome of the greedy procedure. However, note that this is not the point of the approach. The motivation to start with mature neurons is to ask whether adult-born cells can contribute something to decoding, given that mature cells on their own perform better.

Second, the reviewer questions the size of the population that we reach with the greedy procedure. Note that for the population sizes that we show in the manuscript the decoding performance already begins to saturate, Fig. 4F-H. Furthermore, it is unfeasible to construct a 1M neurons population due to the computational cost –the time it takes to run the algorithm. These two facts motivated us to stop at 12 neurons as it strikes a good balance between computational time and saturation. Importantly, as we expand below, the aim of the greedy procedure simulation is not reconstructing the actual network of the dentate gyrus. Rather, we seek to understand whether immature neurons could improve coding in a population.

Third, the reviewer observes that the fraction of adult born cells in the reconstructed populations using the greedy procedure are large as compared to the biological network. Again, here note that the aim of the whole in-silico experiment is not to recover the biological network, where other aspects are at play. More simply, we query the possible contribution of adult born cells to coding. In fact, if we obtained the same proportion it would be by chance, since we do not think that adult-born cells in the dentate gyrus are chosen according to the greedy algorithm.

Still, this comment from the reviewer motivated us to include further simulations of the greedy procedure with constraints. In the revised manuscript we show new results using the greedy procedure, but constraining the fraction of immature neurons in the resulting populations, see Figure 4-figure supplement 2.

More generally, we think that these comments reveal a possible misunderstanding about the approach, its purpose and the interpretation of the results. The point of the greedy procedure is to show that immature neurons do in fact contribute to improve the decoding, despite being generally worse individually. We do not claim that the population obtained with the greedy procedure faithfully reflects the actual shape of the in vivo network. We are aware that it does not. We see that this may have not been clear in the original version. In the revised version, we now explain the purpose of the greedy procedure when we introduced it. Additionally, we comment on the proportion of immature neurons in the same paragraph.

4) Likewise, the idea of dynamic pattern separation seems quite nice. However, the authors focus on the differences between mixed and pure networks, which are extremely small. Furthermore, the correlation coefficients of "low", "medium", and "high" correlation groups are chosen completely arbitrarily. A correlation coefficient of 0.99, considered low here, would seem extremely high in other contexts. Whether dynamic pattern separation is possible over a wider range of input correlation coefficients is unclear (see O'Reilly and McClelland, 1995, Hippocampus, for a possible relationship). Finally, aren't code expansion and lateral inhibition the key mechanisms underlying pattern separation? None of these potential mechanisms are incorporated here.

The reviewer positively appreciates the idea of the pattern separation task that we propose in the manuscript, and poses some questions concerning the extent of the contribution of adult-born neurons.

We agree that code expansion and lateral inhibition are key mechanisms for pattern separation in the DG, and we do not claim that adult-born neurogenesis is the key mechanism behind pattern separation. Rather, in our work we explore the role of adultborn immature neurons in coding in general, and in pattern separation in particular, given that it’s a commonly attributed function to the DG.

We note that the correlation in O'Reilly and McClelland 1994 (actually, what they call pattern overlap) is of a very different nature than the one we compute in our work. They compute the overlap between different patterns of activation in a population of neurons, that is the probability that a single neuron is active in two different patterns of activation. In our manuscript we compute the correlation between different continuous time-varying stimuli that stimulate single neurons.

Importantly, previous work has shown that ablating neurogenesis particularly affects fine spatial discrimination, that is when the separation between patterns is small, but not when it is large (Clelland 2009, Science). Hence, we were actually expecting the impact of adult-born neurons to be important only for relatively large correlation coefficient values.

In the revised manuscript, we now explain the rationale for the choice of correlation values, both in the main text when we introduce the task, and in the Methods when we set the values for the low, medium and high correlation classes. We also added a sentence to the discussion on pattern separation, bringing in the importance of the ideas of lateral inhibition, code expansion, and the work of O’Reilly 1994.

5) A main conclusion of the paper is that while mature GCs are better decoders on the single cell level, heterogeneity in mixtures improves coding in neuronal networks. However, this seems to be true only for r^2 as a readout criterion (Fig. 4F). For information, the result is less clear (Fig. 4G). The results must be discussed in a more objective way. Furthermore, intuitive explanations for this paradoxical observation are not provided. Saying that "this is an interesting open question for future work" is not enough.

This is an interesting point raised by the Reviewer. While r^2 is quantified by comparing the decoded stimuli with the true stimuli, mutual information is related to the uncertainty about the decoding. That is, it quantifies the correspondence between decoded and true stimuli, but does not tell us whether it is a good approximation to it. For example, a decoder could achieve perfect mutual information but result in a poor reconstruction by performing a perfectly scrambled one-to-one mapping of the true stimulus [Schneidman et al. 2003], see also our reply to point [5] by Reviewer #1 above.

We agree that this is an important point and we realize that it was not clear in the original version of the manuscript. In the revised manuscript we added some sentences to clarify this point.

6) The authors ignore possible differences in the output of mature and adult-born granule cells in their thinking. If mature and adult-born granule cells had different outputs, this could affect their contributions to the code (either positively or negatively). At the very least, this possibility should be discussed.

Newborn neurons contact the same targets as mature neurons, born during development: pyramidal cells in CA3, and interneurons in CA3 and the DG. During the maturation, there is a sequence of connectivity with CA3 and within the DG (Toni et a. 2008). At 4 weeks, newborn cells are already contacting their postsynaptic targets. Still, there may be subtle differences in the strength of these connections compared to mature neurons.

So, although the targets are the same, there may be quantitative differences in the way they contribute to the code. Thus the point raised by the reviewer is interesting, so we decided to discuss it further in the revision.

Author Response

Reviewer #1 (Public Review):

This study used intersectional genetic approaches to stimulate a specific brainstem region while recording swallow/laryngeal motor responses. These results, coupled with histology, demonstrate that the PiCo region of the IRt mediates swallow/laryngeal behaviors, and their coordination with breathing. The data were gathered using solid methods and difficult electrophysiological techniques. This study and its findings are interesting and relevant. The analysis (and/or the presentation of the analysis) is incomplete, as there are analyses that need to be added to the manuscript. The interpretation of the data is mostly valid, but there are claims that are too speculative and are not well-supported by the results. The introduction and discussion would benefit from more citations and a deeper exploration of how this study relates to other work - especially a thorough accounting of and comparison to other studies concerning putative swallow gates.

General/major concerns:

The field of respiratory control is far from unified regarding the role of PiCo in breathing or any other laryngeal behaviors. If anything, the current consensus does not support the triple-oscillator hypothesis (in which PiCo is one of 3 essential respiratory oscillators). The name "PiCo", short for "post-inspiratory complex", suggests a function that has not been well-supported by data - it is a putative post-inspiratory complex, at best. I suggest putting this area in context with other discussions i.e. IRt (such as in Toor et al., 2019) or Dhingra et al. 2020 showed broad activation of many brainstem sites at the post-I period (including pons, BotC, NTS)

The reviewer’s comment refers to our previous publication and not the present one. With all due respect to the reviewer, the submitted study investigates PiCo’s involvement in swallow and laryngeal activation and its coordination with breathing.

We did not feel that it is appropriate for us to critique the Dhingra paper in the present study. However, since this seems to be important to this reviewer, we would like to clarify: Because of filter characteristics, and the low temporal and spatial resolution of these field recordings, the approach used by Dhingra is inappropriate for providing insights into the presence or absence of PiCo. We therefore developed an alternative approach, which provides more detailed insights into population activity, the Neuropixel approach. This Neuropixel recording from PiCo (black trace) exemplifies how field recordings (yellow) fail to pick up post-I activity. We could provide many more examples, but as stated above, addressing the study by Dhingra is tangential to the present study.

We would also emphasize that the study by Dhingra was never designed to provide negative evidence, and Dhingra et al. never claimed that their study demonstrates the absence of PiCo. Unfortunately, the data by Dhingra were misinterpreted by Swen Hülsmann in his Journal of Physiology editorial which created considerable confusion, but also sensation in the field. Objectively, Toor et al reproduced the Anderson study in rats as we will elaborate below. Unfortunately, Toor et al added to the confusion, by renaming the PiCo area into IRt. The field of respiration would have also been confused if the first study reproducing the Smith et al. 1991 study in a different rodent species would have refused to call this area preBötC and instead would have called it e.g. ventrolateral reticular field.

Did you perform control experiments in which the opto stimulations were done on animals without the genetic channels (for example, WT or uncrossed ChAT-ires-cre, etc.), or in mice with the genetic channels that weren't crossed (uncrossed Ai32 mice)? If so, please include. If not, why?

Yes, we performed many control experiments. Aside of many recordings in which viral injections were targeted outside PiCo, we also performed optogenetic stimulations in mice lacking channelrhodopsin. We have now added the following statements and supplemental figure.

Optogenetic stimulation in mice lacking channelrhodopsin

Stimulation of PiCo, across all stimulation durations, in 3 Ai32+/+ mice and 4 ChATcre:Vglut2FlpO:ChR2 mice where the ChR2 did not transfect ChATcre:Vglut2FlpO, as confirmed by a post-hoc histological analysis, resulted in no response (Fig. S3).

How do you know that your opto activations simulate physiological activation? First, the intensive optical activation at the stim site does not occur in those neurons naturally.

This seems like a generic critique of the optogenetic approach. In none of the 10,000+ published optogenetic studies is it known to what extent optogenetic activation stimulates exactly the same neurons and the same degree of activity as during a natural behavior. What we know is that PiCo neurons are activated during postinspiration (Anderson et al. 2016) and that optogenetic activation stimulates these neurons and that this activation evokes the same muscles in the same temporal sequence as a water-evoked swallow. We assume that the reviewer’s comment does not intend to imply that “swallows” evoked by nonspecifically stimulating the SLN is more physiological than the optogenetically-evoked swallows of a specific neuron population? From the reviewer’s other comments, it is obvious that the reviewer has no problems with the results of the Toor study that used exclusively SLN stimulations, an approach which is known to be very non-specific.

Doing a natural (water) stim for comparison is good, but it cannot necessarily be directly compared to the opto stim. The water stim would activate many other brainstem regions in addition to PiCo.

Can the reviewer provide any hard evidence that “many other brainstem regions” are activated by water stimulation in comparison to optogenetic stimulation?

A caveat is that opto PiCo stim =/= water stim (in terms of underlying mechanisms) should be included. Second, in looking at the differences between water vs opto swallows in Table S2: it appears that the ChAT animals (S2A) have something weaker than a swallow with opto stim. For the Vglut2 and ChAT/Vglut2 (S2B&C), the opto swallows also aren't as "strong" as the water swallows (the X and EMG amplitudes are smaller). The interpretation/discussion attributes this to the lack of sensory input during opto stim, but does not mention the strong possibility that there is a difference in central mechanisms occurring. It also seems to be dismissed with the characterization of the swallow as "all-or-none" (see note on Fig 3 results).

With all due respect, we are somewhat surprised that the reviewer dismisses the entire paragraph in the discussion that specifically addresses the comparison between water-swallows and PiCo-stimulated swallows. We discussed the possibility that PiCo stimulated swallows may not activate the full pathway/mechanism as does the water swallow. We carefully compared and confirmed that PiCo-stimulated swallows have the same temporal motor sequence of the same muscles as those activated in water swallows. As already stated, it is surprising that the reviewer has no problem with accepting the validity of previously published methods like electrical non-specific stimulations of the cNTS or SLN, a frequently used and accepted model to produce and study swallow.

The writing needs extensive copy editing to improve clarity and precision, and to fix errors.

Thank you for this comment, we have revised and reviewed the writing.

Results/Fig 1: What proportion had no/other motor response (non-swallow, non-laryngeal) to the opto stim? I can extrapolate by subtraction, but it would be nice to see the "no/other response" on the plot.

With all due respect to this reviewer, but it is not possible to address this question. Specifically, it is not possible to know if a “No response” (meaning “no behavioral output” occurred in response to PiCo stimulation), would have resulted in a swallow or laryngeal activation. However, figure 2 contains responses other than swallows, i.e. “non swallows”, which includes both laryngeal activation as well as “no responses” meaning “no behavioral response” in response to PiCo stimulation. This was determined to assess how the respiratory rhythm is affected when a swallow is not produced by PiCo stimulation.

The explanation of genetics is too spread out and confusing. There needs to be more detail about all the genetic tools used, using the standard language for such tools, in one spot. Please also provide a clear explanation of what those tools accomplish. Include a figure if necessary.

We apologize for creating confusion. We added more explanations to the text.

Pick a conventional designator/abbreviation for the different strains, define them in the methods and in the first paragraph of the results section, and use those abbreviations throughout. I think that using ChAT as an abbreviation for your ChAT-ires-cre x Ai32 mice is confusing because it makes it sound like you're talking about the enzyme rather than the specific strain/neurons. Saying "ChAT stimulated swallows... swallows evoked by water or ChAT" makes it sound like the enzyme choline acetyltransferase itself is stimulating swallow. As is convention, pick a more precise abbreviation like ChAT-cre/Ai32 or ChAT:Ai32 or ChAT-ChR2 or ChAT/EYFP. This goes for the other strains as well.

Thank you for pointing this out. To avoid confusion the strains/neurons are now referred to as: ChATcre:Ai32, Vglut2cre:Ai32, and ChATcre:Vglut2FlpO:ChR2

For Fig S2C&D, why does it say mCherry? Isn't it tdTomato? Is it just an anti-ChAT antibody and then the tdTomato Ai65 is only labeling Vglut2? I don't see this in the methods section.

Thank you for pointing this out. We apologize for our mistake, and we have corrected the manuscript to say tdTomato.

I also don't see methods for all the staining in Fig S3. The photomicrograph says Vglut2-cre Ai6, but there's no mention of Ai6 anywhere else. Which mice are these? Did you cross Vglut2-cre with an Ai6 reporter mouse? How can you image an Ai6 mouse (which I assume expresses ZsGreen? and that you excited at 488?) and a 488 anti-goat in the same section (that's the only secondary listed in the methods that would work with your goat anti-ChAT)? Is there an error in listing the fluorophores in the methods? Please give more details on the microscopy including which filters were used for the triple staining.

We have decided to remove the CTb data from the manuscript.

Regarding the staining: I would expect the staining/maps in for the 2 different ChAT/Vglut2 intersectional strains to be similar (Fig 5A/B and S2C/D). The photomicrographs look very different to me, while the heat maps (this goes for all the heat maps in the paper) have barely distinguishable differences. In Fig 5, the staining looks much stronger than in Fig S2C. Why does it look like there are so many more transfected neurons in Fig 5A2 than there are red neurons in the corresponding panel Fig S2C2? And for Fig 5A4 and Fig S2C44? The plot and results text for Fig 5 says the avg number of neurons was 123+¬11. The plot for Fig S2D says 112+¬15, but the results text says 242+¬12 (not sure which is the correct number).

Thank you for your comments. Previously the heat maps had different scale bars if you compare Fig 5A/B and S2C/D (now figure S4C/D). We changed the heat maps keeping the same scale for all of them. Discussing the representative photomicrography, even figure Fig 5A/B and S4C/D represents the same cluster of cells (PiCo Chat/Vglut+). Figure S4D states 242 ± 12 neurons (also stated in the results section).

However, we want to point out that there are several technical differences between both, 1) figure 5A represents the transfection promoted by the virus injection, impacting the number of cells stained/transfected (133 ± 16 neurons), 2) figure S4C/D represents a intersectional mouse ChATcre: Vglut2FlpO: Ai65; (242 ± 12 neurons). In this case, we have more tdTomato positive cells because this genetic approach is able to detect most of the Chat and Vglut2 cells. The difference between figures is considered normal for anatomical studies, in some studies the same bregma can show different number of cells. Thus, the differences are due to the differences in the type of approaches (viral expressions vs. intersectional approach).

We have also added additional experiments to figure 5 (now N=7) which has been reflected in the text and figures.

The results text for Fig S2C also says the staining is "similar to the previous ChAT staining...", which I assume refers to S2A/B. The plot and results text for Fig S2B reports 403+¬39 neurons, while S2D is either 112 or 242 (not sure?). The plots have different Y scales, which should be changed to be the same. But why do the photomicrographs and the heat maps look so similar? I would expect far fewer neurons to be stained in the intersectional mice (Fig 5 and Fig S2C/D) than in the ChAT staining (Fig S2A/B). I am having trouble reconciling the different presentations/quantifications and making sense of the data in these histology figures.

We removed “similar to the previous ChAT staining” and we have reviewed the heat maps. Since the original submission, we performed more experiments and now added more animals to the analysis (now N=7), each heat map represents the correct number of neurons in PiCo, respectively to each experiment.

The Y scales has been adjust to better demonstrate the Chat staining vs. the intersectional mice triple conditioned.

How can you distinguish PiCo from non-PiCo in the histology, especially in the ChAT-only staining? It seems that you have arbitrarily defined the PiCo region, and only counted neurons within that very constrained area.

Even in ChAT-only staining, the N.ambiguus is very distinct from the cholinergic neurons located more medial to the N.ambiguus. This can be unambiguously be confirmed by combining ChAT with glutamatergic in situ staining as done in the Anderson et al. study, or unambiguously be demonstrated with the viral approach as done in the present study. Thus, we don’t see why it is arbitrary to define the distribution of PiCo neurons. What is arbitrary is the definition of the preBötC, yet the field of respiration seems to have no problem with this. We assume that the reviewer knows that Dbx1 neurons are spread along the entire ventral respiratory column and dorsal portion of the PreBötzinger Complex up to the level of the XII nucleus. Yet it is commonly accepted for authors to refer to the PreBötzinger Complex by counting dbx1 neurons within a constrained area of what is believed to be the PreBötzinger Complex, even though the borders are arbitrary. It is e.g. known that some of the ventrally located preBötC neurons are presumed rhythmogenic while the more dorsally located Dbx1 neurons are premotor. The transition from rhythmogenic to premotor is gradual. Similarly, NK1 staining, or SST staining is not restricted to the preBötC and it is arbitrary to define where preBötC begins and what to include. Indeed, our PNAS paper indicates that inspiratory bursts can be generated by optogenetically stimulating Dbx1 neurons along the entire VRC column – so it is not clear where the rhythmogenic portion of the preBötC begins rostrocaudally and dorsoventrally and where the rhythmogenic portion and preBötC itself ends. Thus, we want to re-iterate and emphasize, that for the present study, we developed a method using the cre/FlpO approach to unambiguously define the PiCo region. It is surprising that this reviewer does not acknowledge this technical advance that added significantly more specificity to the anatomical and physiological characterization of PiCo, than the Toor et al. study, and also the Anderson et al. study.

I can see stained neurons in the area immediately outside of PiCo, and I'd like to see lower-magnification images that show the staining distribution in a broader region surrounding PiCo as well, especially in the rest of the reticular formation.

We characterized the PiCo area based on the histological phenotype and in vitro and in vivo experiments performed by Anderson et al., 2016. PiCo is an area located close to the NAmb, presenting the same ChATcre phenotype. As stated above, the distribution and agglomeration of the NAmb is clearly very compact, and different then the observed ChATcre: Vglut2FlpO: Ai65 neurons located outside of NAmb. It is also important to emphasize, that like is the case for the preBötC, other transmitter phenotypes of neurons are also present in the PiCo region (i.e. GABA or Dbx1). However, the study performed by Anderson et al, 2016 paper, described only the functions of cholinergic neurons located in PiCo, and we always planned to publish a paper of the other neurons within PiCo – this area e.g. contains pacemaker neurons etc. But, I hope that the reviewer acknowledges that many investigators have studied the preBötC for the past 30 years. Hence, much more information has been accumulated on this region (which btw was at least as controversial at the beginning), and it will likely take at least another 30 years to fully identify and characterize PiCo.

Similarly, how can you be sure you're stereotaxically targeting PiCo precisely (600um in diameter?) with your opto fiber (200um in diameter). Wouldn't small variations in anatomy put the fiber outside the tiny PiCo area?

We assume the reviewer means “stereotactically”. And yes, the reviewer is correct, it is necessary to position the laser at a consistent anatomical location. Placement of the optical fibers outside of this area does not result in activation of PiCo. We have added an additional supplemental figure (Figure S6) to address this.

Please put N's and stats results in Table S1 for both swallow and laryngeal activity. I took what I assume to be the Ns (10, 11, and 4) and did some stats like the ones you presented for the laryngeal duration. The differences between vagus duration for 40 and 200 ms pulse durations are all significant for each strain, by my calculations. Also, I think there must be an error in the orange swallow plot in Fig 3A. The orange dots don't correspond to the table values. I plotted all the Table S1 values for each strain. Each line looks similar to the blue laryngeal activation plot in Fig 3A. The slopes of the Vglut2 were less than the other strains, and the slopes for the swallow behavior were less than the laryngeal behavior for all strains. Otherwise, they all look similar. Please double-check your values/stats to address these discrepancies. If it is indeed true that the stim pulse duration affects swallow duration, revise the interpretations and manuscript accordingly.

We thank the reviewer for the diligence in reviewing our manuscript. But, with all due respect, the reviewer is incorrect and misunderstood the data. To clarify: Table S1 is only presenting data for laryngeal activation, swallow data is presented in Table S2. The orange data points in Fig 3A are not detailed in Table S1 or S2. Table S2 is the average of all swallows across all laser pulse durations since the laser pulse duration does not affect swallow behavior duration. All data will be publically available after publication of the manuscript.

Figure 3A is only representing the ChATcre:Vglut2FlpO:ChR2 column of Table S1

The N’s have been added to table S1

Please add more details on stats in general, including the specific tests that were performed, F values and degrees of freedom, etc.

Thank you, this has been added throughout the results section. Please refer to the results section for this addition. However below we have provided an example.

An example: A two-way ANOVA revealed a significant interaction between time and behavior (p<0.0001, df= 4, F= 23.31) in ChATcre:Vglut2FlpO:ChR2 mice (N=7).

How do you know that you're not just activating motoneurons in the NA when you stimulate your ChAT animals, especially given the results in Fig 1B? In this case, the phase-specific results could be explained by inhibitory inputs (during inspiration) to motoneurons in the region of the opto stim.

As stated in this paper as well as the Anderson et al 2016 paper (and for that matter also the Toor et al study) this is a caveat. This major caveat motivated the development and use of the ChATcre:Vglut2FlpO:ChR2 (specifically targeting the PiCo neurons that co-express ChAT and Vglut2, not laryngeal motor neurons) experiments that have mostly the same response as the ChATcre:Ai32 mice. We cannot say this is due to inhibitory inputs to laryngeal motoneurons, since the cre/FlpO specific experiments are not directly activating laryngeal motoneurons. But we do not want to entirely exclude that some premotor mechanisms may also occur in PiCo. The reviewer may know that there is overlap of rhythmogenic and premotor functions for the Dbx1 neurons in the PreBötC, But, addressing this issue is beyond the scope of this study. In fact, we are working on a separate connectivity study using novel, still unpublished antegrade and retrograde vectors that do not reveal any direct connections to laryngeal motoneurons. Hence, we expect that the connectivity from PiCo to laryngeal motoneurons is more complex and addressing this question cannot be done as a simple add-on to an already complex study. Again, we would refer to the PreBötzinger complex, where nobody expects that one study can resolve all the physiological and anatomical characterizations that have been accumulated over 30 years in one study. We would argue that in some ways, our cre/FlpO approach is more specific than the Dbx1 stimulations which activates not only rhythmogenetic PreBötzinger complex neurons, but also pre motoneurons as well as glia cells, and many neurons rostral and caudal to the PreBötzinger complex. We are aware of these caveats, and we have discussed this in the original submission, and also in the revision.

While the study from Toor et al is cited, there needs to be a much more thorough discussion of how their findings relate to the current study.

Many thanks for asking for a more thorough discussion of Toor et al., which we are happy to provide here. Perhaps we were too polite in our original manuscript to emphasize all the problems in that study.

They demonstrated that PiCo isn't necessary for the apneic portion of swallow. Inhibiting this region also didn't affect TI.

Please note – the fact that Toor et al did not find an effect on TI confirms Anderson et al. 2016: In Figure 3G,3F of the Nature paper, the reviewer will find that injections of DAMGO and SST into PiCo inhibited post-I activity without affect inspiratory duration. This figure also shows that the inspiratory burst can terminate in the absence of postinspiratory activity.

The reviewer states: “They demonstrated that PiCo isn't necessary for the apneic portion of swallow”. With all due respect to this reviewer, this is NOT correct. Toor et al showed that inhibiting PiCo did block SLN-evoked fictive-swallows but not the apnea caused by SLN stimulation. This is not the apnea caused by swallows (which was never studied by Toor), but by the SLN stimulation. The apnea evoked by SLN stimulation has most likely nothing to do with the apnea caused by swallows. Unfortunately, the Toor et al. makes the same misleading claim as the reviewer.

PiCo cannot be the sole source of post-I timing, and the evidence overwhelmingly favors the major involvement of other regions such as the pons.

This comment seems to be unrelated to the main thrust of this paper that studies PiCo’s involvement in swallow and laryngeal activation in coordination with breathing. However, since this comment seems to discredit the Ramirez lab in general, we would like to clarify that inhibiting PiCo with DAMGO and SST inhibits post-I activity (Anderson et al 2016, Fig.3G,3F). Thus, we don’t understand the rationale or actual data for the reviewer’s conclusion that PiCo cannot be the sole source of post-I timing? We also don’t understand the basis for the reviewer’s conclusion that “the evidence overwhelmingly favors the major involvement of other regions such as the pons”. We also want to add, that no-where in the Anderson et al. study did we state that the pons plays NO role. Indeed, we specifically stated: “In this context it will be interesting to resolve the role of the PiCo in specific postinspiratory behaviors and to identify how the PiCo interacts with other neural networks such as the Kolliker-Fuse nucleus, a pontine structure that has been hypothesized to gate postinspiratory activity and the periaqueductal grey a structure involved in vocalization and the control of postinspiration”.

They also showed that inhibition of all neurons (not just ChAT/Vglut) in the PiCo region suppresses post-I activity in eupnea. This suppression was overcome by the increased respiratory drive during hypoxia.

Before comparisons are made with Toor et al. it is important to note the species and methodological differences between Toor et al. rat anesthetized, vagotomized, paralyzed and artificially ventilated model which evaluated fictive swallows (deafferented and paralyzed). By contrast this study uses a mouse anesthetized, vagal intact, freely breathing model and evaluates natural physiologic swallow via water and central stimulation. It seems that the reviewers does not acknowledge one of the main innovations of this study. For this study we introduced a genetic approach to specifically target and activate ChATcre/Vglut2FlpO PiCo neurons. This has never been done before, and developing this approach took more than 4 years of breeding and crossing and testing different options.

As for Toor et al., these authors pharmacologically, bilaterally inhibited neurons in the area of PiCo with isoguvacine, a specific GABA-A agonist. Even though this pharmacological intervention does not specifically inhibit cholinergic/glutamatergic neurons in PiCo, these authors essentially confirm the study by Anderson et al. We do not find this finding controversial. Perhaps the reviewer finds the definition of PiCo “controversial”, because Toor et al called the identical area IRt instead of PiCo, even though they exactly reproduce the finding by Anderson. Toor et al. not only arrive at the same conclusion as Anderson but they added more details – none of which is contradicting the results by Anderson et al.: Here are excerpts from the Toor study “We therefore conclude that the ongoing activity of neurons in the IRt contributes to eupneic respiratory and sympathetic post-I activities without exerting significant control on other respiratory or cardiovascular parameters” “IRt significantly inhibited the post-I components of VNA” “IRt inhibition was also associated with a reduction in PNA” “increase in respiratory cycle frequency” “due to a reduction in TE“ “with no effect on TI observed”. “Bilateral microinjection of isoguvacine selectively reduced the magnitudes of post-I VNA and rSNA, but not PNA responses to acute hypoxemia”.

In this statement the reviewer probably refers to one particular aspect, i.e. the fact that Toor et al. did not significantly block some of the post-I activity – they state: “had no significant effect on the AUC of post-I rSNA (305+/- 24 vs 230+/- 28,p=0.16,n=6)”. Please note that there is a tendency, a reduction from 305-230. Perhaps the Toor study was not sufficiently powered to fully block the effect, perhaps the drug did not inhibit the entire PiCo. These are all open questions that a critical reader should know. The reviewer will agree that it is as difficult if not more difficult to demonstrate the absence of an effect. To arrive at a negative conclusion experiments should be done with the same scrutiny than to demonstrate a positive result. We also assume that the reviewer is familiar with animal experiments and will understand that pharmacological injections are often difficult to interpret, in particular in case of local in vivo injections. It is possible that Toor et al is inhibiting e.g. parts of the Bötzinger complex.

We have added to the manuscript the following statement: It is important to note that SLN stimulation does not only trigger swallows, but also changes in the overall stiffness and tension of the vocal cords (Chhetri et al., 2013) as well as prolonged hypoglossal activation independent of swallowing (Jiang, Mitchell, & Lipski, 1991). It has been hypothesized that inhibition of the IRt blocks fictive swallow but not swallow-related apnea. Yet this apnea was generated by SLN stimulation and not by a natural swallow stimulation (Ain Summan Toor et al., 2019). It is known that SLN stimulation causes endogenous release of adenosine that activates 2A receptors on GABAergic neurons resulting in the release of GABA on inspiratory neurons and subsequent inspiratory inhibition (Abu-Shaweesh, 2007), suggesting that the SLN evoked apnea may not be the same as a swallow related apnea. Moreover, microinjections of isoguvacine into the Bötzinger complex attenuated the apneic response but not the ELM burst activity (Sun, Bautista, Berkowitz, Zhao, & Pilowsky, 2011), suggesting the Bötzinger complex, not PiCo, could be involved in modulating apnea.

We would also like to add that our current study characterized swallow-related specific muscles and nerves in both water-triggered and PiCo-triggered swallows to better characterize the physiological properties of this swallow behavior. By contrast, Toor et al. only characterized nerve activities that are involved in multiple upper airway activities and breathing. It is somewhat surprising that the reviewer did not consider the fact that Toor et al. characterized putative swallows that were triggered by SLN stimulation and that Toor et al. were content with nerve-recordings and failed to confirm that the behavior that they evoked is actually a physiological swallow. Which, according to the comments from this reviewer (see above), indicates the possibility of differences in central mechanisms occurring between fictive swallow and physiological swallows.

While we have cited Toor et al and their truly excellent work in the broad iRt we did not feel it is appropriate to critique them for the fact that they are confusing the field by using a different anatomical term for the area that was clearly defined by us as an area containing cholinergic-glutamatergic neurons. We also did not feel it is appropriate to discuss results that are similar to comparing Apples and Oranges. Toor et al. never specifically manipulated glutamatergic-cholinergic neurons, thus their entire results rest on indirect stimulation affecting this general area – which will unavoidably also include laryngeal motoneurons. We don’t want to criticize this approach, since PiCo is heterogenous, which is another misunderstanding that we find in the reviewers’ critique. We used cholinergic-glutamatergic neurons to define this area. However, like the preBötC, PiCo is also heterogenous. This region contains inhibitory neurons, it also contains glutamatergic neurons that are not cholinergic, and cholinergic neurons that are not glutamatergic. Because of this heterogeneity we compared the effects of stimulating glutamatergic neurons and cholinergic neurons as well as cholinergic-glutamatergic neurons. This is an approach that is generally accepted in the field. As already stated, there is not a single marker that uniquely characterizes the PreBötC. Thus, when stimulating Dbx1 neurons, glutamatergic neurons, or Somatostatin neurons it only captures subpopulations of this region. The recently published study by Menuet et al. in eLife, used even more indirect methods to inhibit preBötC. They used a pan-neuronal CBA promotor that targets neurons irrespective of phenotype. It is not our intention to discredit this very elegant study, but we object the statement that we “have arbitrarily defined the PiCo region”.

This study has not demonstrated some of the things that are depicted in Fig 7 and included in the discussion. While swallow can inhibit inspiration, there are many mechanisms by which this can happen other than a direct inhibitory connection from the DGS to PreBotC. You cite Sun et al., 2011 findings of "a group of neurons that inhibits inspiration" during SLN stim, but don't mention that it is the BotC and that the paper shows that swallow apnea is dependent on BotC. That is also supported by the Toor study. I don't understand how post-I (aka E) can be discussed without discussion of the BotC - this is a glaring omission.

We have removed figure 7, which was only meant as a hypothetical schematic.

Why is it necessary for PiCo to innervate the cNTS?

This was a hypothesis based on CTb data that we have now removed.

That is true if the conjecture that PiCo gates swallowing is true, as the cNTS is the only known region for central swallow gating. However, PiCo could influence afferent input to the NTS less directly, and therefore not function as a gating hub per se. The experimental evidence does not warrant the claim that PiCo gates swallowing. The definition of a swallow gate(s) is a topic of much debate and no conclusive experimental evidence has emerged for swallow gating regions to exist anywhere except in the NTS. The current study's evidence also does not meet the criteria necessary to conclusively call PiCo a swallow gate. The authors should soften this claim and language throughout the manuscript.

Although we do not know of any studies that has optogenetically gated swallow in the cNTS, it seems the reviewer objects our use of the word “gate”. We have revised the manuscript and removed any wording stating PiCo is a swallow “gate”. It would be interesting to know whether the reviewer has the same objections of the use of the word “relay” as done by Toor et al.?

It is also unclear that PiCo acts directly on the swallow pattern generator to gate swallowing. It is not just "conceivable that the gating mechanism involves" the pons, but nearly certain. Swallow gating by respiratory activity may not be able to be ascribed to one particular location. At a minimum, it likely involves the NTS/DSG, pons, and possibly IRt (inclusive of PiCo). The authors are correct that "further studies are necessary to understand the interaction between PiCo and the pontine respiratory group on the gating swallow and other airway protective behaviors." This is why it shouldn't be stated that "this small brainstem microcircuits acts as a central gating mechanism for airway protective behaviors."

We have removed all language stating PiCo is a swallow gate.

PiCo is likely part of the VSG (and thus the swallow pattern generator). PiCo, as part of the IRt/VSG could indeed be surveilling afferent information and providing output that affects swallow or other laryngeal activation and the coordination of these behaviors with breathing. However, this is not the responsibility of PiCo alone. This role is likely shared by other parts of the SPG, and may require distributed SPG network participation to be functional. If one were to stim other regions of the distributed SPG, similar results might be expected. When Toor et al silenced the PiCo area (and locations that lie at least lightly beyond the borders of what the present study defines as PiCo), stim-evoked fictive swallows were greatly suppressed. However, swallow-related apnea was unaffected. This supports the role of PiCo as a premotor relay for swallow motor activation, but not as the site that terminates inspiration. Therefore, it cannot be called a gate.

We already addressed the issue that Toor never demonstrated that the “swallow-related” apnea was unaffected. Toor et al only demonstrated that the SLN-evoked apneas were unaffected, and their conclusions were only based on nerve recordings under fictive conditions (deafferented and paralyzed). Also, to the best of our knowledge, many aspects of the putative swallow pattern generator that this reviewer mentions are purely hypothetical. However, to avoid further arguments, we have removed the word gate and Figure 7 from this manuscript.

Similarly, Fig 7 does not accurately depict things that are already well-supported by evidence. PiCo should be included as part of the swallow pattern generator (VSG), not as a separate entity acting on it. The BotC and pons are glaring omissions. This study has not demonstrated the labeled inhibitory connection from DSG to PreBotC. The legend states speculations as fact and needs to be dialed way back to either include statements with solid experimental evidence or to clearly mark things as putative/speculative.

We have removed figure 7.

The discussion of expiratory laryngeal motoneurons needs to be expanded and integrated better into the discussion of swallow, post-I, and other laryngeal motor activation. Why can't PiCo just be premotor to ELMs?

If PiCo would “only” or “just” be premotor to ELM then it would not be expected that it could trigger an all-or-none swallow response with a temporal activity pattern similar to the one of a water-evoked swallow. We would also not expect that the activation of the activity pattern is independent of the laser stimulation duration as demonstrated in Figure 3. This was our reasoning why we originally called PiCo a “gate” because at the correct phase it will gate/trigger a complex swallow sequence. But, as stated above, we avoid the word gate in the revised manuscript.

Concerning the discussion of "PiCo's influence as a gate for airway protective behaviors is blurred...": The incomplete swallow motor sequence didn't seem super different in timing or duration compared to the fully transfected animals (comparing plots from Fig 6 to Fig S1, and Table S2 to Table S3. The values for swallow durations (XII and X) for each group for water and opto seem within similar ranges, as do the differences between water & opto-evoked swallows between strains. While the motor pattern is distinctive from the normal swallow, with laryngeal activity rather than submental activity leading, one might not even be able to call that a swallow. Is it evidence against a classic all-or-nothing swallow behavior any more than the graded swallow results from (fully transfected) Table S1?

We fully agree that it is possible that this unidentified behavior may not be a swallow. We have changed the name of this behavior to “upper airway motor activity.” However we also cannot rule out the possibility of this being some portion of a graded swallow which would argue that a graded swallow response is exact evidence against the classic all or nothing swallow behavior.

Please expand on this point and put it into context with others' results: "This brings into question whether this is the first evidence against the classic dogma of swallow as an "all or nothing" behavior, and/or whether this is an indication that activating the cholinergic/glutamatergic neurons in PiCo is not only gating the SPG, but is actually involved in assembling the swallow motor pattern itself."

This has been expanded and included citation of other studies. The following paragraph can be found in the discussion

Swallow has been thought of as an “all or nothing” response as early as 1883 (Meltzer, 1883). Whether modulating spinal or vagal feedback (Huff A, 2020b), central drive for swallow/breathing (Huff, Karlen-Amarante, Pitts, & Ramirez, 2022) or lesions in swallow related areas of the brainstem (Car, 1979; Robert W Doty, Richmond, & Storey, 1967; Wang & Bieger, 1991) swallow either occurred or did not. Swallows are thought to be a fixed action pattern, with duration of stimulation having no effect on behavior duration (Fig. 3) (Dick, Oku, Romaniuk, & Cherniack, 1993). Thus, it was particularly interesting that in instances when few PiCo neurons were transfected, either unilateral or bilateral, an unknown activation of upper airway activity occurred. Motor activity no longer outlasted laser stimulation rather was contained within, and the timing of the motor sequence was reversed in comparison to a water or PiCo evoked swallow (Fig. 6). Thus, if insufficient numbers of neurons are activated, PiCo’s influence to specifically activate swallow or laryngeal activation is blurred, resulting in the uncoordinated activation of muscles involved in both behaviors. This brings possible evidence against the classic dogma of swallow as an “all or nothing” behavior, or the presence of an entirely different behavior. We are not the first to bring possible evidence against the classic dogma, “small swallows” were described but failed to be discovered if this was in-fact a partial or incomplete swallow (Miller & Sherrington, 1915). The SPG is thought to consist of bilateral circuits (hemi-CPGs) that govern ipsilateral motor activities, but receive crossing inputs from contralateral swallow interneurons in the reticular formation, thought to coordinate synchrony of swallow movements (Kinoshita et al., 2021; Sugimoto, Umezaki, Takagi, Narikawa, & Shin, 1998; Sugiyama et al., 2011). Incomplete activation of PiCo activates the muscular components of a swallow, without establishing the coordinated timing and sequence of the pattern. It is possible that PiCo is involved in assembling the swallow motor pattern itself and unilateral activation of PiCo could either desynchronize swallow interneurons or activates only one side of the SPG. Since we did not record bilateral swallow related muscles and nerves this question needs to be further examined.

Reviewer #3 (Public Review):

Huff et.al further characterise the anatomy and function of a population of excitatory medullary neurons, the Post-inspiratory Complex (PiCo), which they first described in 2016 as the origin of the laryngeal adduction that occurs in the post-inspiratory phase of quiet breathing. They propose an additional role for the glutamatergic and cholinergic PiCo interneurons in coordinating swallowing and protective airway reflexes with breathing, a critical function of the central respiratory apparatus, the neural mechanics of which have remained enigmatic. Using single allelic and intersectional allelic recombinase transgenic approaches, Huff et al. selectively excited choline acetyltransferase (ChAT) and vesicular glutamate transporter-2 (VGluT2) expressing neurons in the intermediate reticular nucleus of anesthetised mice using an optogenetic approach, evoking a stereotyped swallowing motor pattern (indistinguishable from a water-induced swallow) during the early phase of the breathing cycle (within the first 10% of the cycle) or tonic laryngeal adduction (which tracked tetanically with stimulus length) during the later phase of the breathing cycle (after 70% of the cycle).

They further refine the anatomical demarcation of the PiCo using a combination of ChAT immunohistochemistry and an intersectional transgenic strategy by which fluorescent reporter expression (tdTomato) is regulated by a combinatorial flippase and cre recombinase-dependent cassette in triple allelic mice (Vglut2-ires2-FLPO; ChAT-ires-cre; Ai65).

Lastly, they demonstrate that the PiCo is anatomically positioned to influence the induction of swallowing through a series of neuroanatomical experiments in which the retrograde tracer Cholera Toxin B (CTB) was transported from the proposed location of the putative swallowing pattern generator within the caudal nucleus of the solitary tract (NTS) to glutamatergic ChAT neurons located within the PiCo. We would like to thank the reviewer for acknowledging the technical advances of the present study and for the positive statements in general.

Methods and Results

The experimental approach is appropriate and at the cutting edge for the field: advanced neuroscience techniques for neuronal stimulation (virally driven opsin expression within a genetically intersecting subset of neurons) applied within a sophisticated in vivo preparation in the anaesthetized mouse with electrophysiological recordings from functionally discrete respiratory and swallowing muscles. This approach permits selective stimulation of target cell types and simultaneous assessment of gain-of-function on multiple respiratory and swallowing outputs. This intersectional method ensures PiCo activation occurs in isolation from surrounding glutamatergic IRt interneurons, which serve a diverse range of homeostatic and locomotor functions, and immediately adjacent cholinergic laryngeal motor neurons within the nucleus ambiguous (seen by some as a limitation of the original study that first described the PiCo and its roll in post-I rhythm generation Anderson et al., 2016 Nature 536, 76-80). These experiments are technically demanding and have been expertly performed.

Again, we would like to thank the reviewer for these positive comments acknowledging the advances of the present study.

The supplemental tracing experiments are of a lower standard. CTB is a robust retrograde tracer with some inherent limitations, paramount of which is the inadvertent labelling of neurons whose axons pass through the site of tracer deposition, commonly leading to false positives. In the context of labelling promiscuity by CTB, the small number of PiCo neurons labelled from the NTS (maybe 5 or 6 at most in an optical plane that features 20 or more PiCo neurons) is a concern. Even assuming that only a small subset of PiCo neurons makes this connection with the presumed swallowing CPG within the cNTS, interpretation is not helped by the low contrast of the tracer labelling (relative to the background) and the poor quality of the image itself. The connection the authors are trying to demonstrate between PiCo and the cNTS could be solidified using anterograde tracing data the authors should already have at hand (i.e. EYFP labelling driven by the con-fon AAV vectors from PiCo neurons (shown in Fig5), which should robustly label any projections to the cNTS).

We fully agree with the reviewer that the CTB staining is of a lower standard and have removed this approach.

The retrograde labelling from laryngeal muscles seems unnecessary: the laryngeal motor pool is well established (within the nAmb and ventral medulla), and it would be unprecedented for a population of glutamatergic neurons to form direct connections with muscles (beyond the sensory pool).

The authors support their claim that PiCo neurons gate laryngeal activity with breathing through the demonstration that selective activation of glutamatergic and cholinergic PiCo neurons is sufficient to drive oral/pharyngeal/laryngeal motor responses under anaesthesia and that such responses are qualitatively shaped by the phase of the respiratory cycle within which stimulation occurs. Optical stimulation within the first 10% of the respiratory cycle was sufficient to evoke a complete, stereotyped swallow that reset the breathing cycle, while stimuli within the later 70% of the cycle, evoked discharge of the laryngeal muscles in a stimulus length-dependent manner. Induced swallows were qualitatively indistinguishable from naturalistic swallow induced by the introduction of water into the oral cavity. The authors note that a detailed interpretation of induced laryngeal activity is probably beyond the technical limits of their recordings, but they speculate that this activity may represent the laryngeal adductor reflex. This seems like a reasonable conclusion.

We thank the reviewer for this comment. Unfortunately, we felt compelled to remove the word “gating” based on the statements by reviewer 1.

The authors propose a model whereby the PiCo impinges upon the swallowing CPG (itself a poorly resolved structure) to explain their physiological data. The anatomical data presented in this study (retrograde transport of CTB from cNTS to PiCo) are insufficient to support this claim. As suggested above, complementary, high-quality, anterograde tracing data demonstrating connectivity between these structures as well as other brain regions would help to support this claim and broaden the impact of the study.

We fully agree with this reviewer. We have been working on a thorough anatomical characterization for more than 3 years using cutting edge anterograde and retrograde viruses in collaboration with vector experts at the University of Irvine. But these are partly novel, unpublished techniques that are in development, and require many careful controls and characterization. We feel that this is a separate study as it doesn’t relate to swallowing coordination and also includes partly different authors. We hope to submit this as a separate study later this year.

This study proposes that the PiCo in addition to serving as the site of generation of the post-I rhythm also gates swallowing and respiration. The scope of the study is small, and limited to the subfields of swallowing and respiratory neuroscience, however, this is an important basic biological question within these fields. The basic biological mechanisms that link these two behaviors, breathing and swallowing, are elusive and are critical in understanding how the brain achieves robust regulation of motor patterning of the aerodigestive tract, a mechanism that prevents aspiration of food and drink during ingestion. This study pushes the PiCo as a key candidate and supports this claim with solid functional data. A more comprehensive study demonstrating the necessity of the PiCo for swallow/breathing coordination through loss of function experiments (inhibitory optogenetics applied in the same transgenic context) along with robust connectivity data would solidify this claim.

Thanks again for the positive assessment of our study.

Author Response

Reviewer #1 (Public Review)

Using in vitro assays that take advantage of thymic slices, with or without the ability to present pMHC antigens, the authors define an early period in which CCR4 expression is induced, which induces their migration to the medulla and likely encounter with cDC2 and other APCs. Notably, the timing for CCR4 expression precedes that of CCR7 and illustrates the potential role for this early expression to initiate the movement of post-positive selection thymocytes to the medulla. The evidence for supporting a role for CCR4, as well as CCR7, in sequential tolerance induction is provided using multiple approaches, and although the observed changes amount to small percent changes, the significance is clear and likely biologically relevant over the lifespan of a developing T cell repertoire. Overall, the model provides a holistic view of how tolerance to self-antigens is likely induced during T cell development, which makes this work highly topical and influential to the field.

We thank the reviewer for their comments and for highlighting the significance of identifying distinct roles for CCR4 and CCR7 in promoting medullary localization and inducing self-tolerance of thymocytes at different stages of T-cell development.

Reviewer #2: (Public Review )

This manuscript describes that CCR4 and CCR7 differentially regulate thymocyte localization with distinct outcomes for central tolerance. Overall, the data are presented clearly. The distinct roles of CCR4 and CCR7 at different phases of thymocyte deletion (shown in Figure 6C) are novel and important. However, the conclusion that expression profiles of CCR4 and CCR7 are different during DP to SP thymocyte development was documented previously. More importantly, the data presented in this manuscript do not support the conclusion that CCR7 is uncoupled from medullary entry. Moreover, it is unclear how the short-term thymus slice culture experiments reflect thymocyte migration from the cortex to the medulla.

We thank the reviewer for pointing out the significance of our finding that CCR4 and CCR7 regulate different phases of thymocyte deletion. We agree that prior reports, including our own (Cowan et al. 2014, Hu et al., 2015) have shown that CCR4 and CCR7 are expressed by different post-positive selection thymocytes. However, the expression data we present here provides a higher resolution perspective on the specific thymocyte subsets that express these two receptors, as well as the different timing with which the receptors are expressed after positive selection. These data, coupled with chemotaxis assays of the granular thymocyte subsets responding to CCR4 versus CCR7 ligands, and 2-photon imaging data showing that CCR4 and CCR7 are required for medullary accumulation of distinct thymocyte subsets, are critical for delineating the unexpectedly distinct roles of these two chemokine receptors in promoting medullary entry and central tolerance.

The reviewer raises an important question about our conclusion that CCR7 is “uncoupled” from medullary entry. We think there was likely a misunderstanding of our intended meaning, as we did not mean to imply that CCR7 does not promote medullary entry of thymocyte subsets; we have modified the wording of the abstract to replace “uncoupled” to clarify. As we detail in the Introduction, the role of CCR7 in directing chemotaxis of single-positive thymocytes towards the medulla and inducing their medullary accumulation is well established (Ehrlich et al., 2009; Kurobe et al., 2006; Kwan & Killeen, 2004; Nitta et al., 2009; Ueno et al., 2004). Instead, our data demonstrate that 1) the most immediate post-positive selection thymocyte subset (DP CD3loCD69+) does not require CCR7 for medullary entry, and 2) the next stage of post-positive selection thymocytes (CD4SP SM) express CCR7, but CCR7 recruits these cells only modestly into medulla. In contrast, CCR7 promotes robust medullary accumulation of more mature thymocyte subsets (CD4SP M1+M2), in keeping with the well-known role of CCR7 in promoting thymocyte medullary localization. We think these findings are highly significant for the field because currently, there is a widely held assumption that post-positive selection thymocytes that do not express CCR7 are located in the cortex, while those that express CCR7 are located in the medulla. Our data show that neither of these assumptions is true: CCR4 drives medullary accumulation of cells that do not yet express CCR7, and the earliest post-positive selection cells that express CCR7 continue to migrate in both the cortex and medulla. These findings form the basis of our statement that CCR7 expression is “not synonymous with” medullary localization. The finding that thymocytes do not robustly accumulate in the medulla in a CCR7-dependent manner until more the mature SP stages has important implications for central tolerance, as localization of thymocytes in the cortex versus medulla will impact which APCs and self-antigens they encounter when testing their TCRs for self-reactivity.

The reviewer also raised concerns about whether short-term thymus slice cultures reflect physiological thymocyte migration. Short-term live thymic slice cultures have been widely used to investigate the development, localization, migration, and positive and negative selection of thymocytes, as they have been shown to faithfully reflect these in vivo processes, including confirming the role of CCR7 in inducing chemotaxis of mature thymocytes from the cortex into the medulla (Au-Yeung et al., 2014; Dzhagalov et al., 2013; Ehrlich et al., 2009; Lancaster et al., 2019; Melichar et al., 2013; Ross et al., 2014). However, we acknowledge that thymic slices are not equivalent to intact thymuses and have now discussed limitations of this system in our revised Discussion.

Comment 1: Differential profiles in the expression of chemokine receptors, including CCR4, CCR7, and CXCR4, during DP to SP thymocyte development were well documented. Previous papers reported an early and transient expression of CCR4, a subsequent and persistent expression of CCR7, and an inverse reduction of CXCR4 (Campbell, et al., 1999, Cowan, et al., 2014, and Kadakia, et al. 2019). The data shown in Figures 1, 2, and 3 are repetitive to previously published data.

The expression profile of CCR4, CCR7 and CXCR4 on thymocytes has been documented previously in the studies cited above and in our prior publication (Hu et al., 2015). Campbell et al. (Campbell, Haraldsen, et al., 1999) investigated chemotactic effects of chemokines, but did not directly address expression of chemokine receptors by thymocyte subsets. Cowan et al. (Cowan et al., 2014) examined the expression of CCR4 versus CCR7 on DP and CD4SP thymocytes. However, our data provide a more detailed analysis of expression of these distinct chemokine receptors by subsets of DP, CD4SP, and CD8SP thymocyte subsets along the trajectory of differentiation after positive selection, using a gating scheme inspired by a study published after the above-cited papers (Breed et al., 2019). Our more nuanced evaluation of CCR4 versus CCR7 expression sets the stage for finding that they play distinct roles in promoting medullary entry and central tolerance of early- versus late-stage post-positive selection thymocytes. Without examining CCR4 and CCR7 expression patterns by distinct thymocyte subsets in detail, we would not have made the unexpected observation that although CCR7 is expressed at high levels by many CD4SP SM thymocytes, it does not induce strong chemotaxis or medullary accumulation of this subset, relative to its role in more mature SP thymocyte subsets. This finding has important implications for which APCs thymocytes encounter as they are tested for self-reactivity to enforce central tolerance. As we were working on these studies, Kadakia et al. reported that extinguishing CXCR4 expression was important for enabling medullary entry (Kadakia et al., 2019). Thus, we thought it was important to place CXCR4 in the context of CCR4 and CCR7 expression on thymocyte subsets in our study, and in doing so found another example of asynchronous chemokine receptor expression and function, further indicating that expression of a chemokine receptor alone is not a reliable marker of functional activity or thymocyte localization, as cells migrate dynamically between the cortex and medulla.

Through more extensive gating and simultaneous investigation of chemokine receptor expression and function, our data have provided new insights into how thymocytes respond to chemokine cues at different time points during their post-positive selection development. Moreover, our refined gating scheme (Figure 1) can be used to distinguish thymocyte subsets at different development stages without relying on chemokine receptor expression, thus providing an unbiased way of investigating chemokine receptor expression at different developmental stages.

Comment 2: The manuscript describes the lack of CCR7 at early stages during DP to SP thymocyte development (Figure 1-3). However, CCR7 expression is detected insensitively in this study. Unlike CCR4 detection with a wide fluorescence range between 0 and 2x104 on the horizontal axis, CCR7 detection has a narrow range between 0 and 2x103 on the vertical axis (Figure 1C, 1D, 4B, 4C, 6B, S2, S3), so that flow cytometric CCR7 detection in this study is 10-times less sensitive than CCR4 detection. It is therefore likely that the "CCR7-negative" cells described in this manuscript actually include "CCR7-low/intermediate" thymocytes described previously (for example, Figure S5A in Van Laethem, et al. Cell 2013 and Figure 6 in Kadakia, et al. J Exp Med 2019).

We provide new data to address the possibility that we were failing to detect low levels of CCR7 expression on early post-positive selection DPs (CD3loCD69+). We agree that CCR7 immunostaining of mouse cells is known to be more challenging than immunostaining of other chemokine receptors, including CCR4 and CXCR4. CCR7 immunostaining needs to be carried out at 37°C, which we did throughout our studies. We provide new data comparing CCR7 expression by Ccr7+/+ versus Ccr7-/- thymocyte subsets (Figure 1—figure supplement 2A-B), which confirm that CCR7 is not expressed at detectable levels by CD3loCD69+ DP cells above the background seen in CCR7-deficient cells. As thymocytes transition to theCD4SP SM stage, low/intermediate to high expression of CCR7 can be detected (Figure 1—figure supplement 2A). To further test whether we were failing to detect low levels of CCR7 by post-positive selection DPs, we incubated thymocytes at 37°C for up to 2 hours prior to immunostaining for CCR4 and CCR7, as a prior study indicated in vitro culture would enable increased cell surface expression of CCR7 by alleviating ligand-mediated CCR7 internalization (Britschgi et al., 2008). However, we did not observe increased CCR7 (or CCR4) expression by any thymocyte subset incubated at 37°C (Figure 1—figure supplement 2C-D). Lack of expression of CCR7 by CD3loCD69+ DP cells is consistent with their failure to undergo chemotaxis to CCR7 ligands in vitro, and initial expression of CCR7 by CD4SP SM is consistent with their chemotaxis towards CCR7 ligands in vitro (now show in greater detail in Figure 2—figure supplement 1), albeit at a much lower migration index than subsequent thymocyte subsets.

Comment 3: Low levels of CCR7 expression could be functionally evaluated by the chemotactic assay as shown in Figure 2. However, the data in Figure 2 are unequally interpreted for CCR4 and CCR7; CCR4 assays are sensitive where a migration index at less than 1.5 is described as positive (Figure 2A and 2B), whereas CCR7 assays are dismissal to such a small migration index and are only judged positive when the migration index exceeds 10 or 20 (Figure 2C and 2D). CCR7 chemotaxis assays should be carried out more sensitively, to equivalently evaluate the chemotactic function of CCR4 and CCR7 during thymocyte development.

We thank the reviewer for his insight about the possibility that we could have overlooked CCR7-mediated chemotaxis at lower migration indexes. When data from the chemotaxis assays were evaluated separately for each thymocyte subset, CCR7-mediated chemotaxis of CD4SP SM and subsequent DP CD3+CD69+ co-receptor reversing thymocytes could be detected. However, DP CD3loCD69+ thymocytes still did not undergo CCR7-meidated chemotaxis, but were responsive to the CCR4 ligand CCL22 (Figure 2—figure supplement 1).

We did not detect CCR7-mediated chemotaxis of CD4SP SM and DP CD3+CD69+ subsets in our previous analysis because their lower-level chemotactic index relative to mature thymocytes did not reach statistical significance when chemotaxis of all subsets were compared simultaneously (Figure 2D). We note that the magnitude of difference in the responsiveness of CD4SP SM cells compared to mature CD4SP and CD8SP M1 & M2 thymocytes (Figure 2D) is likely physiologically important as CCR7 deficiency results in severely reduced medullary accumulation of CD4SP M1+M2 cells, but only a very mild reduction in medullary accumulation of CD4SP SM cells, which is only detected with our new paired analyses in Figure 5C. We feel these new analyses provide important new insights and thank the reviewer for this suggestion.

Comment 4: Together, this manuscript suffers from the poor sensitivity for CCR7 detection both in flow cytometric analysis and chemotactic functional analysis. Conclusions that CCR7 is absent at early stages of DP to SP thymocyte development and that CCR7 is uncoupled from medullary entry are the overinterpretation of those results with the poor sensitivity for CCR7. The oversimplified scheme in Figure 3D is misleading.

We agree that the scheme in Figure 3D, as previously constructed, did not ideally display the difference in scale between thymocyte responses to CCR7 ligands versus CCR4 and CXCR4 ligands (as detected in vitro). Thus, we have now modified the schematic to include the mild response to CCR7 ligands that we observed in CD4SP SM thymocytes (comment 3) and to emphasize the higher chemotactic response of mature thymocytes to CCR7 ligands than of DPs and CD4SP SM to CCR4 ligands. Likewise, we have modified the manuscript to clarify the importance of CCR7 expression in the medullary entry and accumulation of mature thymocyte subsets.

We respectfully disagree that the sensitivity of CCR7 detection was poor in our flow cytometry and chemotactic analyses. Our CCR7 stains identified a range of CCR7 expression levels, from no expression by pre- and post-positive positive selection DP cells to high expression by CD4SP M1 cells, and we now provide new data confirming our ability to detect CCR7 expression (Figure 1—figure supplement 2), as described in response to Comment 3. Our chemotaxis assays detected CCR7 responses over a range of migration indexes from ~ 2 up to 100, showing our sensitive ability to detect CCR7-mediated chemotaxis in vitro (Figure 2 and Figure 2—figure supplement 1). In live thymic slices, we were also able to capture a range of biologic activities of CCR7, from mediating modest medullary accumulation of CD4SP SM cells to robust medullary accumulation of CD4SP M1+M2 cells (Figure 5A-C). Importantly, our results demonstrate that CCR7 is not the only chemokine receptor responsible for medullary entry and accumulation of thymocytes. Complex spatiotemporal regulation of thymocytes at distinct stages of development is achieved through tight orchestration of expression and signaling through multiple chemokine receptors, including CCR4, as shown by our data. However, our study does not negate an important role for CCR7 in mediating medullary entry of thymocytes, which we have clarified in the text.

Comment 5: The short-term thymus slice culture experiments should be described more carefully in terms of selection events during DP to SP thymocyte development, which takes at least 2 days for CD4 lineage T cells and approximately 4 days for CD8 lineage T cells (Saini, et al. Sci Signal 2010 and Kimura, et al. Nat Immunol 2016). The slice culture experiments in this manuscript examined cellular localization within 12 hours and chemokine receptor expression within 24 hours (Figures 4, 5) even for the development of CD8 lineage T cells (Figure S2), which are too short to examine entire events during DP to SP thymocyte development and are designed to only detect early phase events of thymocyte selection.

Experiments in Figures 4 and 5 were indeed designed to capture behaviors of thymocytes relatively early after introduction onto thymic slices. Figure 4 (and Figure 4—figure supplement 1) shows that the timing of CCR4 versus CCR7 expression after positive selection is dramatically different: CCR4 is expressed within hours of positive selection, concomitant with medullary entry, while CCR7 expression takes several days in the slices (sufficient time for CD8SP development, Figure 4—figure supplement 1). Figure 5 shows that medullary accumulation of CD4SP M1+M2 cells occurs robustly in the medulla of thymic slices within a couple of hours after introduction into the slices, and this localization is CCR7 dependent, while CCR4 induces more mild medullary accumulation of post-positive selection DPs. As indicated by the reviewer, it has been shown that it takes days for DP thymocytes to develop into mature CD4SP and CD8SP cells (Kimura et al., 2016; Lutes et al., 2021; Saini et al., 2010), as recapitulated in the thymus slice system (Figure 4—figure supplement 1) (Lutes et al., 2021). The relatively short time frame of our time-course experiments (up to 12 hours after addition of pre-positive selection thymocytes to positively selecting thymic slices) allowed us to detect expression of CCR4 within a few hours after positive selection and to determine that this timing correlated with medullary entry. Thus, the 12-hour time-course was important for temporal resolution of chemokine receptor expression and medullary localization after initial stages of positive selection.

Comment 6: It is unclear what the medullary density alteration measured in the thymus slice culture experiments represents. Although the manuscript describes that the increase in the medullary density reflects the entry of cortical thymocytes to the medulla (Figure 4E and S2E), this medullary density can be affected by other mechanisms, including different survival of the cells seeded on the top of different thymus microenvironments. Thymocytes seeded on the medulla may be more resistant to cell death than thymocytes seeded in the cortex, for example, because of the rich supply of cytokines by the medullary cells. So, the detected alterations in the medullary density may be affected by the differential survival of thymocytes seeded in the cortex and the medulla. Also, the medullary density is measured only within a short period of up to 12 hours. The use of MHC-II-negative slices and CCR4- or CCR7-deficient thymocytes in the thymus slice cultures may verify whether the detected alteration in the medullary density is dependent on TCR-initiated and chemokine-dependent cortex-to-medulla migration.

We thank the reviewer for pointing out these possibilities. The purpose of the positive selection timing experiment (Figure 4) was to establish the early correlation between receiving a positive selection signal, upregulating CCR4, and migrating into the medulla. In this system, cells only enter only the cortex in the first hour after migration in the slice, consistent with prior studies of localization of pre-positive selection thymocytes to the cortex (Ehrlich et al., 2009; Ross et al., 2014); subsequently, they move into the medulla. Because CCR7 is widely accepted to be essential for medullary entry, we feel it is important to demonstrate the disconnect between the timing of medullary entry and CCR7 expression in multiple ways. The timing experiment design utilized MHCII-/- and β2m-/- slices to show that positive selection was necessary for expression of CCR4. To test whether CCR4 or CCR7 were required for medullary entry of early post-positive selection DPs, we evaluated medullary accumulation of this subset from WT, Ccr4-/-, Ccr7-/-, and Ccr4-/-Cc7-/- mice. This experiment provided a more robust means of determining the extent to which CCR4 deficiency impacted medullary localization of a large cohort of cells that had passed positive selection (Figure 5), and again showed that the post-positive selection thymocytes, which express CCR4 but not CCR7, accumulate in the medulla in a CCR4-dependent manner. We note that in Figure 5, we show that all Ccr4-/-Ccr7-/- thymocyte subsets imaged have medullary:cortical density ratios of ~1, indicating an even distribution across cortex and medulla, which is highly consistent with an essential role for these two chemokine receptors in cooperating to mediate medullary accumulation of different stages of developing T cells.

The reviewer makes an interesting point that survival cues could differ in the cortex versus medulla. However, if thymocytes lacking one or both chemokine receptors had impaired survival because they didn’t enter a region of the thymus efficiently to receive survival cues, we would expect to detect increased apoptosis in Ccr4-/-, Ccr7-/-and Ccr4-/-Cc7-/- thymocytes. However, we found that chemokine receptor deficiencies resulted in diminished apoptosis of different thymocyte subsets (Figure 6). This finding is more consistent with reduced negative selection of these subsets due to reduced clonal deletion. We nonetheless discuss this possibility in our revised manuscript, as it important to consider that chemokine-mediated migration of thymocytes into different microenvironments could alter their access cytokines and other pro-survival cues.

Reviewer #3 (Public Review)

In this manuscript, Li et al. examine how the expression of the chemokine receptor CCR4 impacts the movement of thymocytes within the thymus. It is currently known that the chemokine receptor CCR7 is important for developing thymocytes to migrate from the cortical region into the medullary region and CCR7 expression is therefore often used to define medullary localization. This is important because key developmental outcomes, like enforcing tolerance to self-antigens amongst others, occur in the medullary environment. The authors demonstrate that the chemokine receptor CCR4 is induced on thymocytes prior to expression of CCR7 and thymocytes exhibit responsiveness to CCR4 ligands earlier in development. Using elegant live confocal microscopy experiments, the authors demonstrate that CCR4 expression is important for the entry and accumulation of specific thymocyte subsets while CCR7 expression is needed for the accumulation of more mature thymocyte subsets. The use of cells deficient in both CCR4 and CCR7 and competitive migration/accumulation experiments provide strong support for this conclusion. The elimination of CCR4 expression results in decreases in apoptosis of thymocyte subsets that have been signalled through their antigen receptor and are responsive to CCR4 ligands. As expected, more mature thymocyte subsets show decreased apoptosis when CCR7 is absent. Distinct antigen-presenting cells in the thymus express CCR4 ligands supporting a model where CCR4 expressing thymocytes can interact with thymic antigen-presenting cells for induction of apoptosis. The absence of CCR4 results in an increase in peripheral T cells that can respond to self-antigens presented by LPS-activated antigen-presenting cells providing further support for the model. Collectively, the manuscript convincingly demonstrates a previously unappreciated role for CCR4 in directing a subset of thymocytes to the medulla.

We thank the reviewer for appreciating the novelty of the finding that CCR4 directs distinct subsets of thymocytes into the medulla relative to CCR7, as supported by multiple lines of evidence.

Author Response

Reviewer #1 (Public Review):

The sustainability of vaccination programs is subject to multiple threats, from a pandemic like COVID-19 to political changes. The present study assesses different strategies, including gender-neutral vaccination, to better respond to threats in HPV national immunization programs. The authors showed that vaccinating boys against HPV (compared to vaccinating girls alone), would not only prevent more cases of cervical cancer but also limit the impact of disruptions in the program. Moreover, it would help attain the goal set by the World Health Organization of eliminating cervical cancer as a public health problem sooner, even in the case of disruptions.

Strengths and weaknesses: I found the manuscript well-written and easy to read. Decision-makers may find the results helpful in policy development and other researchers may use the study as an example to investigate similar scenarios in their local contexts. Nevertheless, there are some limitations. First, it should be considered that the present study is only applicable to India and other countries with a similar HPV context. Second, because it is a study based on a mathematical model, errors might arise from the assumptions considered for its construction. It also relies on the quality of the data used to construct and calibrate the model.

Models are important tools for decision-making, they allow us to assess different scenarios when obtaining real-world data is not feasible. They also allow to carried-out multiple sensitivity analyses to test the strengths of the results. The study carries out a necessary assessment of different vaccination strategies to minimize the impact on cervical cancer prevention due to disruptions in the HPV immunization program. By using a mathematical model, the authors are able to assess different scenarios regarding vaccination coverage rates, disruption time, and cervical cancer incidence. Therefore, decision-makers can consider the scenario which best represents their current situation.

The present study is not only valuable for decision-making, but also from a methodological point of view as future research can be conducted exploring more in deep the impact of vaccination disruptions and prevention measures.

The conclusions of this paper are mostly well supported by data, but some aspects of the methodology need clarification; furthermore, some aspects of the calculations can be improved. It would be more informative, and better for comparisons between the four scenarios, to have relative measures instead of the absolute numbers of cases prevented.

We thank the reviewer for the kind acknowledgement of the merits of the paper. We have tried to address the suggestions and questions as much as possible in the revised manuscript.

We agree to the points of weaknesses raised by the reviewer regarding the applicability of our study results is limited to other countries and the possible errors arising from a using a mathematical model. We have added more elaborate discussion of these points in the manuscript, as follows: - Page 15 lines 310-312: “Extrapolation of the results of this study to other populations will be limited to those sharing similar patterns of demography, social norms, and cervical cancer epidemiology as India.” - Page 17 lines 361-363: “…, within the limitations of our model, the modelbased estimates show that shifting from GO to GN vaccination may improve the resilience of the Indian HPV vaccination programme while also enhancing progress towards the elimination of cervical cancer.”

Furthermore, we have tried to clarify the rationale, advantages, and limitations of the measure of resilience we have adopted.

Reviewer #2 (Public Review):

This study evaluated the effect of population-based HPV vaccination programs in India which is suffering from the disease burden of cervical cancer. The authors used model simulations for estimating the outcomes by adopting the latest available data in the literature. The findings provide evidence-based support for policymakers to devise efficient strategies to reduce the impacts of cervical cancer in the country.

Strengths.

The study investigated the potential impact of cervical cancer elimination when HPV vaccination was disrupted (e.g., during the COVID-19 pandemic) and for meeting the WHO's initiatives. The authors considered several settings from the low to high effects of vaccination disruption when concluding the findings. The natural history was calibrated to local-specific epidemiological data which helps highlight the validity of the estimation.

Weaknesses.

Despite the importance and strengths, the current study may likely be improved in several directions. First, the study considered the scenario of using a recently developed domestic HPV vaccine but assuming vaccine efficacy based on another foreign HPV vaccine that has been developed and used (overseas) for more than 10 years. More information should be provided to support this important setting.

Second, the authors are advised to discuss the vaccine acceptability and particularly the feasibility to achieve high coverage scenarios in relatively conservative countries where HPV vaccines aim to prevent sexually transmitted infection. Third, as the authors highlighted, the health economics of gender-neutral strategies, which is currently missing in the manuscript, would be a substantial consideration for policymakers to implement a national, population-based vaccination program.

We thank the reviewer for the kind acknowledgement of the merits and strengths of the paper.

We have tried to address the reviewer’s three points of weaknesses as comprehensively as possible in the revised manuscript.

Regarding the first two points of weaknesses, we have provided more background information about the current situation of HPV introduction and screening in India (see the more specific replies below for where changes have been made), and some data of observed coverage in India in the states where HPV vaccination has been introduced.

Regarding the reviewer’s third point about the health economics of genderneutral strategies, we agree fully that it is an important aspect to consider for the local policymakers. However, a health economic assessment is out of the scope of the present paper. In the present paper, we are interested in highlighting the potential health benefits on GN HPV vaccination. Given the current context of HPV vaccination in India we think it is too early to provide a realistic assessment of the health-economic balance of GN vaccination. Please note that one manuscript (de Carvalho et al., MedRxiv, doi: https://doi.org/10.1101/2023.04.14.23288563) based on the same modelling exercise and reporting a health economic assessment of girls-only (routine and catch-up) HPV vaccination in India is currently submitted for peer-review.

Reviewer #3 (Public Review):

The authors put together a rigorous study to model the impact of HPV vaccine programme disruptions on cervical cancer incidence and meeting WHO elimination goals in a low-income country - using India as an example. The study explores possible scenarios by varying HPV vaccination strategies for 10-year-old children between a) increasing vaccine coverage in a girls-only vaccination programme and b) vaccinating boys in addition to girls (i.e a gender-neutral vaccination programme).

The main strength of this study is the strength of the modelling methodology in helping to make predictions and in contingency planning. The study methodology is rigorous and uses models that have been validated in other settings. The study employs a high level of detail in calibrating and adapting the model to the Indian context despite poor data availability. The detailed methodology allows future studies to employ the model and techniques with locally-contextualised parameters to study the potential impact of HPV vaccine programme disruptions in other countries.

The work in this field can begin to help lower-income countries explore varying HPV vaccination strategies to reduce cervical cancer incidence, keeping in mind the potential for future supply chains or other related disruptions. However, the scenarios could be better sculpted to model potentially realistic scenarios to guide policymakers to make decisions in situations with limited vaccine supplies - in other words comparing scenario alternatives based on a fixed number of vaccines being available. Using comparative alternatives will help policymakers grapple with the decisions that need to be made regarding planning national HPV vaccination programmes. The results could afford to provide readers with a clearer measure of vaccine strategy 'resilience'.

In all, the authors are able to successfully explore the potential impact of varying HPV vaccination strategies on cervical cancer cases prevented in the context of vaccine disruptions, and make valid conclusions. The results produced are rich in information and are worthy of deeper discussion.

We thank the reviewer for the kind acknowledgement of the merits and strengths of the paper.

I LOVE scientific-based information, especially when it comes to study techniques/effective ways to learn, so this is really helpful for me! I'll definitely be implementing these into my study habits in the future.

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Reply to the reviewers

Manuscript number: RC-2023-01910

Corresponding author(s): Michael W. Sereda

1. General Statements

Reviewer #1:

In this paper the authors report a direct correlation between PMP22 and PTEN expression levels in the nerve of CMT mutants. In CMT1A Pmp22tg rat nerves, PTEN levels are increased, whereas in Pmp22+/- mutants, a model of the HNPP neuropathy, PTEN levels decrease. Consistent with this, Pmp22tg nerves display lower Akt phosphorylation and, vice versa, Pmp22+/- nerves have higher Akt phosphorylation. The authors lowered PTEN in the transgenic and inhibited mTOR using Rapamycin in the Pmp22+/- to support the functional relevance of the PMP22-PTEN correlation. ... In conclusion, the correlation between PMP22 and PTEN is a potential interesting observation. However, in my opinion, experiments as shown don't support the conclusion that PMP22 controls PTEN expression level and activity, which is suggested at the basis of the pathogenesis of PMP22 dosage-related neuropathies.

We thank Reviewer #1 for this detailed feedback. We appreciate the Reviewer’s assessment that our observation that PMP22 and PTEN are correlated in CMT1A and HNPP is of potential interest. In the revised manuscript we addressed this key point by adding additional quantifications (Figure 1a, d; Figure 5d) and novel Western Blot analyses (Figure 1a, d). Regarding the pathophysiological significance of the correlation, we point out that both the original as well as the partially revised manuscript contain multiple pieces of evidence demonstrating that altered PTEN activity is critical for both PMP22 gene-dosage related neuropathies:

1. The inhibition of the PI3K/PTEN/AKT/mTOR axis upstream (LY294002) or downstream (Rapamycin) of decreased PTEN ameliorates myelin defects in an in vitro HNPP model (Figure 2b, c).
2. Downstream of PTEN, Rapamycin treatment ameliorates myelin defects, motor behavior and electrophysiology in the HNPP mouse model in vivo (Figure 3c, d, e,____ g, i)
3. Targeting of increased PTEN directly by inhibiting its activity pharmacologically (VO-OHpic) in a CMT1A rat model or by depleting it genetically in a CMT1A model leads to ameliorated myelination in vitro (Figure 4b, c; Figure 5f, g).
4. The genetic depletion of PTEN in a CMT1A mouse model increases myelination in vivo, albeit not in the long term (Figure 6a, b, c, d). We therefore feel that any additional evidence to show that "PMP22 controls PTEN activity" is not vital for supporting the major claims of the manuscript, i.e. that the observed correlation of PTEN levels with PMP22 gene dosage has relevance for the etiology of PMP22 dosage diseases and and that targeting the PI3K-PTEN-AKT-mTOR axis downstream of PTEN provides a potential pharmacological therapy of HNPP (while directly targeting PTEN ultimately fails to rescue CMT1A). However, we agree that the activity of PTEN on the molecular level is interesting, and such evidence would further strengthen our conclusions. Therefore, in the final revised version, we plan to add further Western Blots and explore possible downstream effects of altered PTEN levels.

Reviewer #2:

This study investigates the modulation, both genetically and pharmacologically, of the PI3K/Akt/mTOR signaling in preclinical animal models for the inherited peripheral neuropathies HNPP and CMT1A. These conditions result from a gene dosage abnormality of the peripheral myelin protein gene PMP22. The exact biological molecular mechanisms remain enigmatic despite it having been over 30 years since the major genetic lesions, the CMT1A duplication and HNPP deletion, were described. With respect to myelin biology one observes focally slowed nerve conduction at pressure palsies and local/segmental hypermyelination in HNPP whereas hypomyelination occurs in CMT1A. The study is nicely conducted, data illustrations very informative, and writing clear and concise. This paper will likely be of great interest to your readers. The authors provide convincing evidence that the HNPP pathobiology is ameliorated by PI3K/Akt/mTOR inhibitors. Interestingly they found radial myelin growth was most affected by this approach and suggest an interesting transdermal approach in injured nerves in the acute prevention of pressure palsies.

We thank Reviewer #2 for this positive evaluation.

Reviewer #3:

*In this paper Sareda and co-workers demonstrate that the PTEN/mTOR pathway is indirectly involved in regulating myelin thickness and wrapping in models of altered PMP22 gene dosage both in vitro and in vivo. Inhibition of this pathway decreases myelin thickness in models of HNPP, while increasing myelin thickness in models of CMT1A. The evidence for these conclusions is complex but reasonably presented, and the conclusions mainly supported by the data. The abstract for this paper, however, presents a somewhat oversimplified conclusion that the PTEN pathway mainly modifies models of HNPP, where the paper clearly demonstrates that models of CMT1A are also affected by this same pathway. This should be clarified. *

We thank Reviewer #3 for the feedback on the manuscript. We agree with the Reviewer that the same pathway (PI3K/Akt/mTOR) also affects CMT1A, but it is of importance for us to highlight that the disease mechanisms are -at least partly- different between HNPP and CMT1A. This is supported by our observation that PTEN reduction in CMT1A only transiently improves myelination in vivo (Figure 6) and the persistent alteration of differentiation markers despite PTEN reduction, which is not observed in HNPP (Figure 7).

2. Description of the planned revisions

Reviewer #1

Regarding the activity of PTEN

Figure 1

• Additional experiments are needed to support the conclusion of Figure 1 that, in the two mutants, Pten levels reversely correlate with PI3K-Akt-mTOR pathway activation, which represents the rationale of all further experiments. For example, it should be shown systematically in both mutants both Akt and ERK phosphorylation levels (Akt at both T308 and S473), and mTOR activity read outs. In the previously published paper (Fledrich et al.) only increased Akt phosphorylation in Pmp22+/- nerves was reported, whereas Pmp22tg analysis was focused on the interdependence between Akt and ERK without exploring mTOR activation, which is relevant here. 2) (Figure 4) A different model, the C61 mouse a Pmp22tg overexpressing PMP22 is used here (rather than the CMT1A rat). This should be explained in the results. Is also this model characterized by increased Pten levels in the nerve? And low Akt-mTOR activation for instance? 3) (Figure 5) How is Akt-mTOR signaling in the double mutant as compared to Pmp22tg? Is that increased at P18? * Response: We fully agree with the Reviewer that further exploration of PTEN downstream effects will add value to the manuscript. We already justified the usage of the C61 mouse model more clearly, added P-S6 staining of wildtype in addition to an improved representation in Figure 5e, and performed extra Western Blot analysis of PTEN expression (described in the next section “Incorporated *revisions”). Moreover, we will further evaluate the downstream signaling components of PTEN and will perform additional Western Blot analyses of peripheral nerves of HNPP mice, CMT1A rats as well as C61 and C61xPTENhKO mice.

Figure S1

• *Figure S1, page 4: what does it mean "in line with this finding we were unable to detect protein-protein...". May be the authors meant: since there is a direct correlation between Pmp22 and Pten expression levels in the mutants, the authors explored the possibility of an interaction between the two. Regarding the co-IPs, in panel a, the co-IP at the endogenous level, the immunoprecipitation efficiency of PMP22 is very low. May be a pull-down experiment using either exogenous purified PMP22 or PTEN and nerve lysates can help to rule out the possibility of an interaction. The experiments in b, c are performed in overexpression in a heterologous system (293 cells). * Response: We agree with the Reviewer that we might have missed a possible interaction between PMP22 and PTEN in the experiments performed so far. Indeed, pull-down experiments may prove helpful to rule out / reveal protein-protein interaction. Therefore, we will use purified PMP22 and perform pull-down experiments using nerve lysates of wildtype and CMT1A rats.

Figure 5

• *Pten Fl/+ Dhh-Cre cultures seem to have axonal fasciculation. * Response____: We thank the Reviewer for this observation. We will systematically inspected all recorded images for features of fasciculation. We will also assess whether fasciculation is a representative feature in cultures derived from any of the genotypes, and if so, whether the genotypes differ in this regard.

3. Description of the revisions that have already been incorporated in the transferred manuscript

Changes in the text are highlighted in green in the revised manuscript

Reviewer #1:

Figure 1

• *Panel a: the decrease of Pten expression should be quantified with at least n=3 taking into account the variability among different samples at the different time points indicated (the same applies in panel b, even if here the increase of Pten expression level in Pmp22tg nerves is more evident). * Response: We agree with the Reviewer that the timeline is not sufficient to demonstrate alteration in PTEN expression in PMP22 gene dosage diseases CMT1A and HNPP. Therefore, we performed new Western Blot experiments evaluating PTEN expression in (i) HNPP mice, (ii) CMT1A rat (iii) C61 mice and (iv) C61xPTENhKO mice with minimum n = 3 biological replicates and performed the respective quantification which is shown in Figure1 (i, ii) and Figure 5 (iii, iv). The results of the Western Blot analysis and quantification show an increase in PTEN abundance in CMT1A rat (Figure 1d) and C61 mice (Figure 5d) while a decrease is observed in HNPP mice (Figure 1a) and PTENhKOxC61 mice (Figure 5d) when compared to wildtype controls.

• *Panel a and b: the statement that Pten is more expressed at P18 at the peak of myelination in wildtype nerves is not supported by the blots as shown. * Response: We agree that this observation is only partly supported by the Western Blot analysis, as seen in the HNPP mouse model, and deleted this part in the results section.

• Figure S1, page 4: what does it mean "in line with this finding we were unable to detect protein-protein...". May be the authors meant: since there is a direct correlation between Pmp22 and Pten expression levels in the mutants, the authors explored the possibility of an interaction between the two. Response: We thank the Reviewer for pointing out the lack of clarity here. We changed the respective sentence accordingly:

“Since there is a direct correlation between PMP22 and PTEN expression levels in the mutants, we explored the possibility of an interaction between the proteins. By immunoprecipitation experiments we were unable to detect protein-protein interaction between PMP22 and PTEN (Figure S1).” (Page 4)

• *Page 4: "Taken together, Pmp22 dosage inversely correlates with the abundance of PTEN...": please revise this statement * Response: We thank the reviewer for spotting this mistake. We changed the sentence accordingly, which now reads:

“Taken together, Pmp22 dosage directly correlates with the abundance of PTEN and presumably the activation level of the PI3K/Akt/mTOR pathway in myelinating Schwann cells (Figure 1i)." (Page 4, Line 23)

Figure 2:

• The aberrant myelin figures displayed are similar to myelin ovoids preceding degeneration rather than myelin outfoldings. It is also strange that these alterations are in the wildtype cultures treated with RAPA, that instead, in this system, has been reported to increase myelination as it improves protein homeostasis (autophagy, quality control, etc). Response: We thank the Reviewer for pointing this out. Indeed, in the way the images have been presented the aberrant myelin profiles can be mistaken for ovoids. However, a close inspection of the TUJ1 channel images revealed continuity of the axons below the aberrant myelin, thereby excluding ovoid formation. In the partially revised manuscript, we now also show the TUJ1 channel individually (Figure 2), so that it can be appreciated that the defects are confined to the myelin. Concerning the incidence of the myelin defects in RAPA treated wildtype cultures, our analysis can have missed a potential amelioration due to the rather high variability in the data.

Figure 3

*Panel c-e: aberrant fibers should be normalized on total number of fibers and on the area, particularly because RAPA is used. *

Response: We agree with the Reviewer that number of tomacula and recurrent loops should be normalized to the total number of fibers on the area. We have quantified the total number of fibers in the whole sciatic nerve and normalized the tomacula and recurrent loops number accordingly. Results show a decrease in both tomacula and recurrent loops after Rapamycin treatment in the HNPP mice (Figure 3c, d, e, f).

Figure 4

The improvement in the number of myelin segments following PTEN inhibition in Pmp22tg co-cultures is very weak. The 500 nM has instead a consistent effect in reducing myelin segments in the wildtype and I think that these results overall don't support the conclusion that myelination is ameliorated by reducing PTEN activity in Pmp22tg co-cultures.

Response: We thank the Reviewer for this important point. We like to emphasize that we treated whole cultures with the PTEN inhibitor and we cannot rule out a (probably) negative effect on axonal PTEN, resulting in only weak improvement of myelination in PMP22tg cultures and strong effects also on the wildtype co-cultures. Therefore, we decided against a treatment of CMT1A models in vivo and further explored the effects of PTEN reduction specifically in Schwann cells using the genetic model as described Figure 5. The Reviewer made clear to us that this is inappropriately explained in the results section and we therefore adapted this in the manuscript on page 6:

“Similarly, the prolonged inhibition of PTEN with VO-OHpic (for 14 days) caused a dosage-dependent reduction in myelinated segments in wildtype co-cultures (Figure 4c, Figure S2). The mechanism is currently unexplained but cannot rule out a negative effect of PTEN inhibition on DRG neurons and myelination.”

Figure 5:

• *A different model, the C61 mouse a Pmp22tg overexpressing PMP22 is used here (rather than the CMT1A rat). This should be explained in the results. Is also this model characterized by increased Pten levels in the nerve? And low Akt-mTOR activation for instance? * Response: We agree with the Reviewer that it has not been clear in the text why we changed here to the C61 mouse model. We clarified this in the Results section which now reads on page 6:

“To reduce Pten function in CMT1A models also in vivo, we applied a genetic approach (Figure 5a). As the genetic tools to specifically target Schwann cells were only available in the mouse and not the rat, we used the C61 mouse model of CMT1A. We reduced PTEN by about 50% selectively in CMT1A Schwann cells by crossbreeding Pmp22 transgenic mice with floxed Pten and Dhh-cre mice, yielding PTENfl/+Dhhcre/+PMP22tg experimental mutants (Figure 5b). Western blot analyses of sciatic nerve lysates confirmed the increase of PTEN in PMP22tg mice and the reduction of PTEN in the double mutants (Figure 5c, d).”

Moreover, regarding the PTEN expression we added Western Blot analysis and quantification in Figure 5c, d showing increased PTEN expression in the C61 mouse model of CMT1A and decreased PTEN in the PTENhKOxC61 double mutants. Further analysis of the downstream signaling is planned (see “planned revision”).

• *PTEN, Akt-mTOR expression/activation levels should be checked biochemically also in this model. And quantified (panel c). * Response: We added an explanation for the use of the C61 mouse model (see point Figure 5.1 above). Moreover, we quantified the Western Blot analysis and added it in Figure 5d. The expression of PTEN was included in the Western Blot analysis (Figure 5c) showing increased PTEN expression also in the C61 mouse model. Further biochemical analysis of the C61 mouse model is planned (see “planned revision”).

• *In panel d overactivation of mTOR (PS6 staining) in Schwann cells is not evident. * Response: We agree with the Reviewer that the way the image was displayed is not sufficient to show P-S6 activation in the double mutants. We have now split the image (Figure 5e) to better visualize the P-S6 staining alone compared to the co-staining with P0 (marker for compact myelin) and DAPI (nuclei). Further, we added staining of wildtype nerve. We hope this way the differences in P-S6 activation can be easier appreciated.

Figure 6:

*G-ratio analysis: which are the mean values (numbers) with SEM in the three groups analyzed wildtype, Pmp22tg and Pmp22tg; Pten fl/+; Dhh-Cre? *

Response: We thank the Reviewer for pointing this out. We added the quantification of the mean g-ratios in Figure 6d, f.

Figure 7:

• *If more fibers are committed to myelinate in the double mutant as compared to the single Pmp22tg at P18 ,particularly, it is unclear why there is no difference in differentiation marker expression in Figure 7 (Oct6 and Hmgcr). * Response: We thank the reviewer for this comment. We do not necessarily expect to see a strong difference in the expression of differentiation markers given the mild increase in myelination in the double mutants. Similarly, we do not observe alterations in the expression of differentiation markers in HNPP mice, while these fibers produce more myelin. Therefore, we concluded that alterations in PTEN-PI3K/Akt/mTOR signaling do not influence differentiation in the mouse models while in the PMP22 overexpressing situation of CMT1A other mechanisms alter differentiation of the Schwann cells. We also note that experiments were performed at postnatal day 18 and we cannot rule out possible alterations in differentiation marker expression at earlier time points in development in the double mutants.

• In conclusion, the correlation between PMP22 and PTEN is a potential interesting observation. However, in my opinion, experiments as shown don't support the conclusion that PMP22 controls PTEN expression level and activity, which is suggested at the basis of the pathogenesis of PMP22 dosage-related neuropathies. Response: Please also see section 1. In order to avoid any overstatement that "PMP22 controls PTEN expression level and activity", in our revised version we have clarified this point and changed the wording in the main text:

"The mechanisms that link the abundance of PMP22 to that of PTEN are still unclear and we here neither show direct nor indirect control of PTEN expression by PMP22." (Page 8)

Reviewer #2:

1. Regarding in the Introduction: "...the molecular mechanisms causative for the abnormal myelination remain largely unknown and still no therapy is available." Suggest consider modifying to perhaps: '...no small molecule or pharmacological therapeutic intervention exist.' To say "no therapy" exist is 'myopic' and untrue.

*Suggest adding question mark to end of sentence or changing ‘asked’ to “investigated” for following thought: “Here, we asked whether PI3K/Akt/mTOR signaling provides therefore a therapeutic target to treat the consequences of altered Pmp22 gene-dosage.” *

Rather than attempt to establish PRIORITY perhaps ‘softening’ the INTRODUCTION concluding statement “Our results thus identify a potential pharmacological target for this inherited neuropathy.

[This makes thePI3K/Akt/mTOR pathway a promising target for a preventive treatment of affected nerves also in human patients.] *Does this belong in RESULTS? Or rather DISCUSSION? *

Response: We thank the Reviewer for the suggestions. We changed the sentences accordingly in the manuscript (1.: Page 3, Line 23; 2.: Page 3, Line 26; highlighted in green). Regarding point 3, we are convinced that identifying pharmacological targets for peripheral neuropathies should be given priority. Indeed, the aspect concerning point 4 is already highlighted in the discussion therefore we removed the sentence from the result section.

Reviewer #3:

*The abstract for this paper, however, presents a somewhat oversimplified conclusion that the PTEN pathway mainly modifies models of HNPP, where the paper clearly demonstrates that models of CMT1A are also affected by this same pathway. This should be clarified. *

We agree with the Reviewer that the same pathway (PI3K/Akt/mTOR) also affects CMT1A, but it is of importance for us to highlight that the disease mechanisms are -at least partly- different between HNPP and CMT1A. This is supported by our observation that PTEN reduction in CMT1A only transiently improves myelination in vivo (Figure 6) and the persistent alteration of differentiation markers despite PTEN reduction, which is not observed in HNPP (Figure 7). For clarification we have altered the wording in the abstract which now reads: "In contrast, we found that CMT1A pathogenesis was only transiently ameliorated by altered PI3K/Akt/mTOR signaling, which drives radial but not longitudinal growth of peripheral myelin sheaths".

3. Description of analyses that authors prefer not to carry out

Reviewer #1:

Figure 1:

*Figure 1, Panel e: may be with this experiment the authors aim to suggest that Pten and Pmp22 are unlikely to interact directly or indirectly since Pten is cytosolic and Pmp22 myelin-membrane enriched. However, this myelin purification shows that Pmp22 as P0 expression levels are also abundant in the cytosol, may be also because P18 has been chosen as time point. What about a different type of membrane-cytosol fractionation experiment and/or another time point? *

Response: We want to clarify that in this experiment not myelin and cytosol fractions were separated but myelin and whole sciatic nerve lysate (which is the input before isolation of the myelin fraction, called “lysate”). Therefore, the analysis aimed at showing an enrichment of PMP22 and P0 in the myelin fraction while PTEN and TUJ (as a control) are not, which makes it more unlikely for PTEN and PMP22 to interact directly. This experiment, together with the immunohistochemical analysis in Figure 1h should highlight the location of PMP22 and PTEN in the Schwann cell. Together with the newly suggested experiments of the Reviewer for Figure S1 (see planned Revision point 1) we do not see the need for extra membrane-cytosol fractionations and/ or another timepoint as the more detailed as the improved experiment on protein-protein interaction using nerve lysate (not only cell culture) is the experiment of choice to clarify whether we have a direct interaction or not.

Regarding in vitro Schwann cell- DRG co-culture experiments:

(Figure 2, Figure 4 and Figure 5e)

1. *(Figure 2) For this experiment, pulse treatment may be beneficial rather than in continuous. Is Akt-mTOR phosphorylation-signaling increased also in Pmp22+/- co-cultures as in mutant nerves? Is the treatment reducing the overactivation? *
2. *(Figure 4) Similarly to Figure 2, is PTEN level increased in Pmp22tg cultures along with Akt-mTOR downregulation? *
3. *(Figure 5) Panel e: co-cultures are established using ex vivo Dhh-Cre recombination. The downregulation of Pten in the cultures should be documented. * Response: We agree with Reviewer #1 that a deeper analysis of the co-culture system regarding the downstream signaling of PTEN would increase the value of the experiments. Unfortunately, the experiments were designed in a very small scale with the intention of only evaluating myelin alterations on a histological level and we did have enough tissue to collect cells for deeper protein expression analysis. Moreover, we tried to use the co-culture system as a proof-of-principle experiment in parallel to our in vivo studies which we value more important due to the still quite artificial co-culture setup. We hope that the Reviewer can understand our approach with the focus we set on the in vivo work.

Figure 3:

1. *The RAPA treatment seems to increase Pten level in the mutant even above wildtype levels (panel b), which can result in decreased myelin thickness due to downregulation of Akt-mTOR. A different method to normalize expression levels should be used. * Response: Comparing the mean, relative expression levels resulting from our quantification as plotted in the graph (panel b) revealed no increase above wildtype level after Rapamycin treatment in the HNPP mouse. Further, we decided for whole protein staining as the superior approach to loading control because we have observed alterations in the expression of other frequently used “housekeepers” such as GAPDH, Actin and Vinculin in the CMT1A rodent models.

*Panel c-e: Can these data also be reproduced in quadriceps nerves as tomacula are more prominent in these Pmp22+/- nerves showing less variability due to the prevalence of large caliber axons? *

Response: Unfortunately, quadriceps nerves were not collected for histology in the experiment and therefore we cannot redo the quantification. Nevertheless, we agree that the quadriceps nerves have less variability than the sciatic nerve and will definitely include the tissue in our future experiments.

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Referee #1

Evidence, reproducibility and clarity

In this paper the authors report a direct correlation between PMP22 and PTEN expression levels in the nerve of CMT mutants. In CMT1A Pmp22tg rat nerves, PTEN levels are increased, whereas in Pmp22+/- mutants, a model of the HNPP neuropathy, PTEN levels decrease. Consistent with this, Pmp22tg nerves display lower Akt phosphorylation and, viceversa, Pmp22+/- nerves have higher Akt phosphorylation. The authors lowered PTEN in the transgenic and inhibited mTOR using Rapamycin in the Pmp22+/- to support the functional relevance of the PMP22-PTEN correlation.

I have major concerns on the data as shown, which, in my opinion, don't support the main conclusion of this paper. In more detail:

Figure 1 Panel a: the decrease of Pten expression should be quantified with at least n=3 taking into account the variability among different samples at the different time points indicated (the same applies in panel b, even if here the increase of Pten expression level in Pmp22tg nerves is more evident) Panel a and b: the statement that Pten is more expressed at P18 at the peak of myelination in wildtype nerves is not supported by the blots as shown

Figure S1, page 4: what does it mean "in line with this finding we were unable to detect protein-protein...". May be the authors meant: since there is a direct correlation between Pmp22 and Pten expression levels in the mutants, the authors explored the possibility of an interaction between the two. Regarding the co-IPs, in panel a, the co-IP at the endogenous level, the immunoprecipitation efficiency of PMP22 is very low. May be a pull-down experiment using either exogenous purified PMP22 or PTEN and nerve lysates can help to rule out the possibility of an interaction. The experiments in b, c are performed in overexpression in a heterologous system (293 cells).

Panel e: may be with this experiment the authors aim to suggest that Pten and Pmp22 are unlikely to interact directly or indirectly since Pten is cytosolic and Pmp22 myelin-membrane enriched. However, this myelin purification shows that Pmp22 as P0 expression levels are also abundant in the cytosol, may be also because P18 has been chosen as time point. What about a different type of membrane-cytosol fractionation experiment and/or another time point?

Page 4: "Taken together, Pmp22 dosage inversely correlates with the abundance of PTEN...": please revise this statement

Additional experiments are needed to support the conclusion of Figure 1 that, in the two mutants, Pten levels reversely correlate with PI3K-Akt-mTOR pathway activation, which represents the rationale of all further experiments. For example, it should be shown systematically in both mutants both Akt and ERK phosphorylation levels (Akt at both T308 and S473), and mTOR activity read outs. In the previously published paper (Fledrich et al.) only increased Akt phosphorylation in Pmp22+/- nerves was reported, whereas Pmp22tg analysis was focused on the interdependence between Akt and ERK without exploring mTOR activation, which is relevant here.

Figure 2 The aberrant myelin figures displayed are similar to myelin ovoids preceding degeneration rather than myelin outfoldings. It is also strange that these alterations are in the wildtype cultures treated with RAPA, that instead, in this system, has been reported to increase myelination as it improves protein homeostasis (autophagy, quality control, etc). Also for this experiment, pulse treatment may be beneficial rather than in continuous. Is Akt-mTOR phosphorylation-signaling increased also in Pmp22+/- co-cultures as in mutant nerves? Is the treatment reducing the overactivation?

Figure 3 The RAPA treatment seems to increase Pten level in the mutant even above wildtype levels (panel b), which can result in decreased myelin thickness due to downregulation of Akt-mTOR. A different method to normalize expression levels should be used. Panel c-e: aberrant fibers should be normalized on total number of fibers and on the area, particularly because RAPA is used. Can these data also be reproduced in quadriceps nerves as tomacula are more prominent in these Pmp22+/- nerves showing less variability due to the prevalence of large caliber axons?

Figure 4 A different model, the C61 mouse a Pmp22tg overexpressing PMP22 is used here (rather than the CMT1A rat). This should be explained in the results. Is also this model characterized by increased Pten levels in the nerve? And low Akt-mTOR activation for instance?

The improvement in the number of myelin segments following PTEN inhibition in Pmp22tg co-cultures is very weak.. The 500 nM has instead a consistent effect in reducing myelin segments in the wildtype and I think that these results overall don't support the conclusion that myelination is ameliorated by reducing PTEN activity in Pmp22tg co-cultures. Similarly to Figure 2, is PTEN level increased in Pmp22tg cultures along with Akt-mTOR downregulation?

Figure 5 As for Figure 4, the use of the mouse transgenic instead of the CMT1A rat should be specified and PTEN, Akt-mTOR expression/activation levels should be checked biochemically also in this model. And quantified (panel c). In panel d overactivation of mTOR (PS6 staining) in Schwann cells is not evident. Panel e: co-cultures are established using ex vivo Dhh-Cre recombination. The downregulation of Pten in the cultures should be documented. Pten Fl/+ Dhh-Cre cultures seem to have axonal fasciculation.

Figure 6 G-ratio analysis: which are the mean values (numbers) with SEM in the three groups analyzed wildtype, Pmp22tg and Pmp22tg; Pten fl/+; Dhh-Cre? How is Akt-mTOR signaling in the double mutant as compared to Pmp22tg? Is that increased at P18? If more fibers are committed to myelinate in the double mutant as compared to the single Pmp22tg at P18 ,particularly, it is unclear why there is no difference in differentiation marker expression in Figure 7 (Oct6 and Hmgcr).

Significance

In conclusion, the correlation between PMP22 and PTEN is a potential interesting observation. However, in my opinion, experiments as shown don't support the conclusion that PMP22 controls PTEN expression level and activity, which is suggested at the basis of the pathogenesis of PMP22 dosage-related neuropathies.

Author Response:

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

We are very glad that the editor and reviewers found our paper of broad interest to the community of population, evolutionary, and ecological genetics. We thank them for their positive feedback and insightful comments and suggestions. We have revised our manuscript to address some of the issues raised by the review. The main change we made was providing a detailed discussion of limitations of simulated genomes, focusing on considerations one needs to make when selecting a demographic model. This can be found in a new section “Limitations of simulated genomes” (pages 9-10). We made a few additional adjustments in other parts of the text based on the reviewers’ suggestions. They are all listed in the detailed point-by-point response to reviewers comments and questions below.

Editor:

1) It was noted that demographic models (or genomic parameters) that are inferred based on certain aspects of the genomic data (eg., site frequency spectrum, haplotype structure) may not recapitulate other aspects of the data. In other words, any inferred demographic models are expected to reliably reproduce only some aspects of the genetic variation data but not necessarily all. It would be helpful to emphasize this limitation in the manuscript and to include a table summarizing the types of variation that the demographic models for the catalogued species were based on.

This is a very important point, which we addressed in the revision by adding a section entitled “Limitations of simulated genomes”. This section discusses the considerations that one should make when selecting an inferred demographic model to implement in simulation. This includes the samples used in analysis, the method used for inference, as well as various filters. In this section we also point to the documentation page of the stdpopsim catalog, which provides information about each demographic model that can help users decide whether it is appropriate for their needs. We decided not to summarize this information in a succinct table in the manuscript because it is not straightforward to summarize the strengths and potential limitations of each model in a table. Instead, we will expand the summary provided for each demographic model in the documentation page to provide additional information. See response to the second reviewer’s comment on this topic for more details.

2) It will make stdpopsim more user-friendly to include an automated module that can visualize a demographic model given the corresponding parameters (or simulation scripts).

As mentioned in the response to the first reviewer’s comment on this subject, the documentation page of the stdpopsim catalog provides a brief summary for each demographic model, including a graphical representation. See response below for more details.

Reviewer #1:

In the introduction, the authors cite numerous efforts to generate high-quality reference genomes. That's not an issue in itself, but leading with this might send the message to some readers that it is these reference genome efforts that are driving the need for population genomics analysis and simulation tools, which is not really the case - why not instead give some citation attention to actual population genomics projects aiming to address the types of evolutionary questions this paper is concerned with? The reference genome citations would fit better in the section dealing with reference genomes, where they already appear.

Indeed, the desire to answer complex evolutionary questions is the main motivation for sequencing these genomes and also for generating realistic genome simulations. The reason we chose to lead with the genome-sequencing efforts is that high quality genome data is an important prerequisite for obtaining parameters for chromosome-scale simulations. So, with that perspective, these efforts which we cite are the driving force behind expansion of stdpopsim in the near future. Thus, we decided to leave these citations in the introduction. To balance things out, we now start the introduction with a statement about board questions in population genetics. Moreover, after we list the genome sequencing efforts, we added a list of specific types of questions that can be addressed by these newly emerging genomes, with relevant citations. The beginning of the introduction now reads:

“Population genetics allows us to answer questions across scales from deep evolutionary time to ongoing ecological dynamics, and dramatic reductions in sequencing costs enable the generation of unprecedented amounts of genomic data that can be used to address these questions (Ellegren, 2014). Ongoing efforts to systematically sequence life on Earth by initiatives such as the Earth Biogenome (Lewin et al., 2022) and its affiliated project networks, such as Vertebrate Genomes (Rhie et al., 2021), 10,000 Plants (Cheng et al., 2018) and others (Darwin Tree of Life Project Consortium, 2022), are providing the backbone for enormous increases in the amount of population-level genomic data available for model and non-model species. These data are being used, among other things, in inference of population history and demographic parameters (Beichman et al., 2018), studying adaptive introgression (Gower et al., 2021), distinguishing adaptation from drift (e.g. Hsieh et al., 2021), and understanding the implications of deleterious variation in populations of conservation concern (e.g. Robinson et al., 2023).”

Something that would be useful for the stdpopsim resource in general, though not necessarily something for the paper, would be some kind of more human-friendly representation of the demographic models implemented in the curated library. Perhaps I'm not looking in the right place, but as far as I can tell, if I want to study the curated demographic models, I need to go into the Python scripts on the stdpopsim GitHub page (e.g.

https://github.com/popsim-consortium/stdpopsim/tree/main/stdpopsim/catalog/BosTau). Here the various parameters and demographic events are hard-coded into the scripts. To understand the model being implemented, one thus needs to go dig into these scripts - something which is not necessarily very accessible to all researchers. Visual representations, such as the one for Anopheles gambiae in Fig 2. in the paper, are more widely accessible. I wonder if such figures could be produced for all the curated models and included in the GitHub folders alongside the scripts, perhaps aided by an existing model visualization software such as POPdemog. Again, I would not suggest that this is necessary for the paper, but if practically feasible I think it would be a useful addition to the resource in the longer term.

This is a very good point. The stdpopsim catalog actually has a documentation page that provides a brief summary for each demographic model, including a graphical representation. This graphical representation is generated using demesdraw applied to the demographic model object implemented in the code. Thus, potential users do not have to dig through the Python code to figure out the details of the demographic model. We used a similar approach to generate the image of the demographic history of A. gambiae for Fig. 2 of the paper. The documentation page is an important part of the stdpopsim catalog, and we now added a link to it in section “Data availability”, and we mention it in key places in the manuscript, such as the caption of Fig 2.

Reviewer #2:

An important update to the stdpopsim software is the capacity for researchers to annotate coding regions of the genome, permitting distributions of fitness effects and linked selection to be modeled. However, though this novel feature expands the breadth of processes that can be evaluated as well as is applicable to all species within the stdpopsim framework, the authors do not provide significant detail regarding this feature, stating that they will provide more details about it in a forthcoming publication. Compared to this feature, the additions of extra species, finite-site substitution models, and non-crossover recombination are more specialized updates to the software.

It would be helpful to provide additional information regarding the coding annotation (and associated distribution of fitness effects and linked selection) that is implemented in the current version of stdpopsim, but will be detailed in a forthcoming paper. This is not to take away from the forthcoming paper, but I believe this is the most important update to the software, and the current manuscript only brushes over it.

We agree that implementation of selection in simulations is a significant addition to stdpopsim. However, our intention in this manuscript is to focus on the separate effort we made in the last two years to expand the utility of stdpopsim to a more diverse set of species. We think the manuscript stands firmly even without discussing in detail the new features that allow modeling selection. The main reason we briefly mention these features in sections “Additions to stdpopsim” and “Basic setup for chromosome-level simulations” is because the released version of stdpopsim contains implemented DFEs for a few species, and we did not want to completely ignore this. We thus added a brief comment at the end of the “Basic setup” section (page 8) mentioning the three model species for which the stdpopsim catalog currently has annotations and implemented DFE models. We think that a more detailed description of how these features and how they should be used is best left to the manuscript that the PopSim community is currently writing (preprint expected later this year).

When it comes to simulating realistic genomic data, the authors clearly lay out that parameters obtained from the literature must be compatible, such as the same recombination and mutation rates used to infer a demographic history should also be used within stdpopsim if employing that demographic history for simulation. This is a highly important point, which is often overlooked. However, it is also important that readers understand that depending on the method used to estimate the demographic history, different demographic models within stdpopsim may not reproduce certain patterns of genetic variation well. The authors do touch on this a bit, providing the example that a constant size demographic history will be unable to capture variation expected from recent size changes (e.g., excess of low-frequency alleles). However, depending on the data used to estimate a demographic history, certain types of variation may be unreliably modeled (Biechman et al. 2017; G3, 7:3605-3620). For example, if a site frequency spectrum method was used to estimate a demographic history, then the simulations under this model from y stdpopsim may not recapitulate the haplotype structure well in the observed species. Similarly, if a method such as PSMC applied to a single diploid genome was used to estimate a demographic history, then the simulations under this model from stdpopsim may not recapitulate the site frequency spectrum well in the observed species. Though the authors indicate that citations are given to each demographic model and model parameter for each species, this may not be sufficient for a novice researcher in this field to understand what forms of genomic variation the models may be capable of reliably producing. A potential worry is that the inclusion of a species within stdpopsim may serve as an endorsement to users regarding the available simulation models (though I understand this is not the case by the authors), and it would be helpful if users and readers were guided on the type of variation the models should be able to reliably reproduce for each species and demographic history available for each species. It would be helpful to include a table with types of observed variation that the current set of 21 species (and associated demographic histories) are likely and unlikely to recapitulate well.

This is a very important point, which we now address in the section “Limitations of simulated genomes”, which we added to the manuscript. In this section, we expand on this topic and discuss various things that will affect the way simulated genomes reflect true sequence variation. This includes the choice of demographic inference method, but also the analyzed samples, and various filters. The main message of this section is that one should consider various things when deciding to implement a demographic model in simulation (or selecting a model among those implemented in stdpopsim). We also cite studies (including Beichman, et al. 2017), which compared different approaches to demography inference. However, we note that the conclusions of these comparisons are not as straightforward as the reviewer suggests. In particular, methods that make use of the site frequency spectrum (such as dadi) should be able to capture some aspects of haplotype structure, because this information is encoded in the demographic history. Furthermore, a demographic history inferred from a single genome (e.g., using PSMC) should do a reasonable job approximating some aspects of the site frequency spectrum. In other words, the aspects of genetic variation not modeled well by a given demographic inference method are not always predicted in a straightforward way. This is why we avoid summarizing this information in a table in the manuscript. The 2nd paragraph of the “Limitations of simulated genomes” section addresses some of these subtle considerations. In particular, we suggest that considering a demographic model for simulation requires some familiarity with the inference method and the way it was applied to data. Regarding the demographic models currently implemented in stdpopsim, we provide some information about each model in the documentation page of the catalog. When selecting a demographic model from the catalog, users should make use of this documentation to guide their decision. This is mentioned in the 3rd paragraph of the “Limitations of simulated genomes” section. Following-up on this issue, we intend to review the documentation and make sure it provides sufficient information for each demographic model. See this GitHub issue.

Reviewer #3:

- p5, 2nd paragraph: I think many Biologists, myself included, will think of horizontal gene transfer mostly as plasmids being transferred among bacteria and adding extra genetic material, not as homologous bacterial recombination. This made me confused about modelling horizontal gene transfer in the same way as gene conversion. It may be helpful for some readers if you specify that you are modelling this particular type of horizontal gene transfer. Some explanation along the lines of what is in Cury et al (2022) would be enough.

This is a good point. We modified the text in that sentence in the 2nd paragraph on page 5 to clarify that we are modeling non-crossover homologous recombination, and not incorporation of exogenous DNA (e.g., via plasmid transfer). The relevant part of the text now says:

“In bacteria and archaea, genetic material can be exchanged through horizontal gene transfer, which can add new genetic material (e.g., via the transfer of plasmids) or replace homologous sequences through homologous recombination (Thomas and Nielsen, 2005; Didelot and Maiden, 2010; Gophna and Altman-Price, 2022). However, the initial version of stdpopsim used crossover recombination to stand in for these processes. Although we cannot currently simulate varying gene content (as would be required to simulate the addition of new genetic material by horizontal gene transfer), the msprime and SLiM simulation engines now allow gene conversion, which has the same effect as non-crossover homologous recombination.

Following (Cury et al., 2022), we use this to include non-crossover homologous recombination in bacterial and archaeal species.”

- p5, 3rd paragraph: When you say gene conversion is turned off by default, you could refer to table 1 and briefly mention the consequence of ignoring gene conversion.

We agree that it is important to note that avoiding to model gene conversion may lead to faulty lengths of shared haplotypes across individuals. This is implied by the statement we make in the beginning of the 3rd paragraph on page 5, where we lay out the motivation for modeling gene conversion in simulation. Following the reviewer’s suggestion, we now added a statement about this in the end of that paragraph:

“Note that ignoring gene conversion may result in a slightly skewed distribution of shared haplotypes between individuals (see Table 1)”

-  p7, item 1 and p9, 1st paragraph: I am not sure what you mean by genetic map here, can you define this term? I am not sure if it is synonymous with gene annotations, a recombination map, or something else. The linkage map doesn't seem to make sense to me here.

The term ‘genetic map’ referred to the recombination map whenever it was used in the manuscript. To avoid any confusion, we now removed all mentions of ‘genetic map’, and use ‘recombination map’ instead. The recombination map is relevant in item 1 of page 7 because in species with poor assemblies you will not be able to reliably estimate recombination maps, making chromosome-scale simulations less effective. In the 1st paragraph of page 9, we discuss the issue of lifting over coordinates from one assembly to another, and if you have a recombination map estimated in one assembly, you might need to lift it over to another assembly to apply it in your simulation.

-  Table 1, last row, middle column: when you say "simulated population", I think it is a bit ambiguous. You mean "the true population that we are trying to simulate", but could be read as "the population data that was generated by simulation". I would delete the word simulated here.

What we mean here is that the selected effective population size should reflect the observed genetic diversity in real genomic data. We realize that the previous wording was confusing, and changed this to the following:

“Set the effective population size (Ne) to a value that reflects the observed genetic diversity”

-  Figure 2, and other places when you refer to mutation and recombination rate (eg p11, last paragraph), can you include the units (e.g. per base pair, per generation)?

Throughout the manuscript, rates are always specified per base per generation. In Figure 2, this is specified in the caption (3rd line). We added units in other places in section “Examples of added species” on pages 12-13, where they were indeed missing.

-  p11, "default effective population size": can you use a more descriptive word instead of the default? Maybe the historical average? Also, what is this value used for in the simulations when there is a demographic model specified (as in the case of Anopheles)?

We think that “default effective population size” is the most appropriate term to use here, since we are referring to the parameter in the species model in stdpopsim. It is correct that the value of this parameter should reflect the historical average size in some sense, but it is really unclear what this should be in the case of a species like Bos taurus, which experienced a very dramatic bottleneck in the recent past. We address this subtle, yet important, issue in the sentence preceding this one. If a demographic model is specified in simulation, it overrides the default effective population size, and its value is ignored (which is why we refer to it as ‘default’). We added a short sentence clarifying this in the 2nd paragraph of the “Bos Taurus” section (now page 12).

“Note that the default Ne is only used in simulation if a demographic model is not specified.”

-  p8, when you say "Such simulations are useful for a number of purposes, but they cannot be used to model the influence of natural selection on patterns of genetic variation.": You may want to bring up the discussion that many of these neutral parameters taken from the literature could have been estimated assuming genome-wide neutrality, and thus ignoring the effect of background selection. Therefore the parameter values might reflect some effect of background selection that was unaccounted for during their estimation.

This is an important subtle point, which we now address in the section “Limitations of simulated genomes”, which we added to the revised manuscript. In that section, we discuss various limitations of simulations, focusing on inferred demographic models. We address the potential influence of the segments selected for analysis toward the end of 2nd paragraph in that section (page 9):

“... all methods assume that the input sequences are neutrally evolving. This implies that technical choices, such as the specific genomic segments analyzed and various filters, may also influence the inferred model and its ability to model observed genetic variation.”

Interestingly, background selection in itself typically does not have a strong effect on the inferred model. This is something that is examined in the forthcoming publication that presents simulations with natural selection in stdpopsim.

-  Why are some concepts written in bold (eg effective population size, demographic model)? Were you planning to make a vocabulary box? I think this is a good idea given that you are aiming for a public that can include people who are not very familiar with some population genetics concepts.

In the “Examples of added species” section, we use boldface fonts to highlight the model parameters that were determined for each species. We added a statement clarifying this in the beginning of this section (page 11), and made sure that all the relevant parameters were consistently highlighted throughout this section. In other sections, we use boldface fonts only for titles. A few cases that did not conform to this rule were removed in the current version. We did not intend on adding a vocabulary box, but considered this when revising the manuscript, due to the reviewer’s suggestion. However, we found it difficult to converge on a small (yet comprehensive) set of terms with accurate and succinct definitions. We think that the important terms are adequately defined within the text of the manuscript, providing sufficient information also for readers who are not expert population geneticists.

- p4, 2nd paragraph: Are these automated scripts that are used to compare models publicly available? If you are suggesting that people use this approach generally when coming up with a simulation model (p8, penultimate paragraph), it would be helpful to have access to these automated scripts.

The scripts are part of the public stdpopsim repository on GitHub, and may be used by anyone. Some components of these scripts are more easy to apply in general, such as comparing a demographic model with one implemented separately by the reviewer. This step, for example, is achieved by application of the Demography.is_equivalent method in msprime. Other parts of the comparison depend on the specific structure of python objects used by stdpopsim, so they are not likely to be useful when implementing simulations outside the framework of stdpopsim.

-  p9, 1st paragraph, and p.12 2nd paragraph: instead of adjusting the mutation rate to fit the demographic model (and using an old estimate of the mutation rate), would it be ok to adjust the demographic model to fit the new mutation rate? E.g. with a new mutation rate that is the double of a previous estimate, would it be ok to just divide Ne by 2 such that Ne*mu is constant (in a constant population size model)? I imagine this could get complicated with population size changes.

In principle, this could be done if you were simulating neutrally evolving sequences (without modeling natural selection). Since the coalescence is scale-free, then you can scale down all population sizes and divergence times by a multiplicative factor, and scale up migration rates and the mutation rate by the same factor, and you get the exact same distribution over the output sequences. However, making sure you get the scaling right is tricky and is quite error-prone. Especially considering the fact that you have to do this every time the mutation rate of a species is updated. Moreover, once you start modeling natural selection, this scale-free property no longer holds. Thus, the simple solution we came up with in stdpopsim is to attach to each demographic model the mutation rate used in its inference.

Author Response:

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

We sincerely thank all the editors and reviewers for taking the time to evaluate this study. Here is our point-by-point response to the reviewers’ comments and concerns.

Reviewer #1 (Public Review):The study by Oikawa and colleagues demonstrates for the first time that a descending inhibitory pathway for nociception exists in non-mammalian organisms, such as Drosophila. This descending inhibitory pathway is mediated by a Drosophila neuropeptide called Drosulfakinin (DSK), which is homologous to mammalian cholecystokinin (CCK). The study creates and uses several Drosophila mutants to convincingly show that DSK negatively regulates nociception. They then use several sophisticated transgenic manipulations to demonstrate that a descending inhibitory pathway for nociception exists in Drosophila.

[…]

Weaknesses:

A minor weakness in the study is that it is unclear how DSK negatively regulates nociception. An earlier study at the Drosophila nmj shows that loss of DSK signaling impairs neurotransmission and synaptic growth. In the current study, loss of CCKLR-17D1 in Goro neurons seems to increase intracellular calcium levels in the presence of noxious heat. An interesting future study would be the examination of the underlying mechanisms for this increase in intracellular calcium.

We thank the reviewer for the kind and very positive evaluation of our manuscript. We agree that this study has not elucidated the intracellular molecular pathway(s) downstream of CCKLR-17D1 that are involved in the regulation of the activity of Goro neurons, and we think that it would definitely be an interesting topic for future research.       

Reviewer #1 (Recommendations For The Authors):

The response latencies for the control yw larvae seem large, with many larvae appearing to be insensitive to the thermal stimulus. Is this just an effect of the yw genetic background? A brief discussion of this might be helpful.

We thank the reviewer for pointing this out. We have also noticed that the yw control larvae tend to show longer response latencies than the other control strains, and in the revised manuscript, we have added the following sentence in the Result section (Lines 91–94):

“We have noticed that the yw control strain, which was used by us to generate the dsk and receptor deletion mutants, showed relatively longer response latencies to the 42 °C probe compared to the other control strains used in this study. This may be attributed to the effect of the genetic background, although, presently, the cause for this difference is unknown.”

Reviewer #2 (Public Review):_

This is an exceptional study that provides conclusive evidence for the existence of a descending pathway from the brain that inhibits nociceptive behavioral outputs in larvae of Drosophila melanogaster. […] The study raises many interesting questions for future study such as what behavioral contexts might depend on this pathway. Using the CAMPARI approach, the authors do not find that the DSK neurons are activated in response to nociceptive input but instead suggest that these cells may be tonically active in gating nociception. Future studies may find contexts in which the output of the DSK neurons is inhibited to facilitate nociception, or contexts in which the cells are more active to inhibit nociception._

Reviewer #2 (Recommendations For The Authors):I have no recommendations for the authors as this is a very complete and thoroughly executed study. The writing is crystal clear.

We thank the reviewer for the kind and very positive evaluation of our manuscript. We are happy to know that our current manuscript was deemed to be clear and convincing by the reviewer.

Reviewer #3 (Public Review):[…] Overall the authors use clean logic to establish a role for DSK and its receptor in regulating nociception. I have made a few suggestions that I believe would strengthen the manuscript as this is an important discovery.

Major comments:

1. It's not completely clear why the authors are staining animals with an FLRFa antibody. Can the authors stain WT and DSK KO animals with a DSK antibody? Also, can the authors show in supplemental what antigen the FLRFa antibody was raised against, and what part of that peptide sequence is retained in the DSK sequence? This overall seems like a weakness in the study that could be improved on in some way by using DSK-specific tools.

We thank the reviewer for this query. We would like to clarify that we first tried the FLRFa antibody to visualize an RFamide-type neuropeptide other than DSK in Drosophila and found that the staining pattern is quite similar to that of anti-DSK, as shown by Nichols et al. [1]. According to the original paper describing the anti-FLRFa antisera [2] (already cited in the reviewed manuscript), the antigen used to raise it was the Phe-Met-Arg-Phe-NH2 peptide conjugated with succinylated thyroglobulin, and the study experimentally shows that the antibody well binds to peptides containing Met-Arg-Phe-NH2 or Leu-Arg-Phe-NH2 sequence and has 100% cross-reactivity to FLRFa. As DSK contains Met-Arg-Phe-NH2 sequence [3], the cross-reaction of this antibody to DSK is consistent with the description of the original study.    

Although we were unable to use an antibody specific to DSK, our staining data with dsk deletion mutants and the expression pattern of DSK-2A-GAL4 corroborate each other (Figure 2 and Figure 2-figure supplement 1), which we believe provides compelling evidence for the specific expression of DSK in MP1 and Sv neurons, and for that DSK-2A-GAL4 is a reasonably effective tool to specifically manipulate DSK-expressing neurons.

2. What is the phenotype of DSK-Gal4 x UAS-TET animals? They should be hyper-reactive. If it's lethal maybe try an inducible approach.

We thank the reviewer for this question. Unfortunately, we have not attempted this experiment, although we agree that this would be a nice addition to further strengthen the study if TET worked well in the DSKergic neurons.

3. Figure 9. This was not totally clear, but I think the authors were evaluating spontaneous (i.e. TRPA1-driven) rolling at 35C. The critical question is "does activating DSK-expressing neurons suppress acute heat nociception" and this hasn't really been addressed. The inclusion of PPK Gal4 + DSK Gal4 in the same animal kind of clouds the overall conclusions the reader can draw. The essential experiment is to express UAS-dTRPA1 in DSK-Gal4 or GORO-Gal4 cells, heat the animals to ~29C, and then test latency to a thermal heat probe (over a range of sub and noxious temperatures). Basically prove the model in Figure 10 showing ectopic activation or inhibition for each major step, then test heat probe responses.

We thank the reviewer for suggesting ideas for alternative experiments to potentially strengthen our conclusion. Regarding experiments using heat probes, previous studies have demonstrated that (i) Blocking ppk1.9-GAL4-positive C4da neurons almost completely abolishes the larval nociceptive response to local heat stimulations [4]; (ii) Local heat stimuli above 39 °C readily activate C4da neurons and larval nociceptive rolling [5-9]; and (iii) Thermogenetically or optogenetically activating these neurons is sufficient to trigger Goro neurons and larval rolling [4, 10-12]. Thus, it has now been made clear that heat probes induce larval nociceptive rolling via excitation of the C4da pathway, and we believe that our experiments using thermogenetic activation of C4da neurons can be safely interpreted as an alternative to experiments using heat probes. Using heat probes demands a more complicated experimental set-up to be combined with CaMPARI imaging experiments, and this is another reason why we preferred to take the thermogenetic approach.

We have also considered the experiment using Goro-GAL4 instead of ppk-GAL4. However, if dTRPA1 artificially activates Goro neurons far downstream of the neuronal mechanism by which MP1 activation suppresses Goro neuron activity, the effect of MP1 activation may be bypassed and masked. As we currently do not know the epistasis between dTRPA function and the effect of MP1 activation in modulating the activity of Goro neurons, we rather chose to activate C4da neurons by using ppk-GAL4, which likely resulted in more natural activation of Goro neurons than dTRPA1-triggered direct activations.

4. It would also then be interesting to see how strong the descending inhibition circuit is in the context of UV burn. If this is a real descending circuit, it should presumably be able to override sensitization after injury.

Indeed, this is an interesting avenue to explore in future studies to understand the type of situation in which the DSKergic descending system functions to control nociception.

Reviewer #3 (Recommendations For The Authors):Overall this is a good story and the claims are generally supported with experimental evidence. The way to really improve this study would be to use more precise and definitive tools, like specific antibodies, specifically targeted genes, and better temporal control of the descending circuit to prove this is inducible sufficient to suppress acute thermal nociception and this occurs only via a descending pathway, etc. However this would be exponentially more work, and so the authors I guess need to weigh the cost-benefit of definitive proof vs. strong evidence for their claims. Overall I think this study will be the beginning of a new line of inquiry in the field that has the potential to guide our understanding also of mammalian descending pathways, and as such, this study is of value to the community.

We appreciate the reviewer’s multiple interesting ideas for experiments that could have been performed to further reinforce our findings. We agree that some experiments that the reviewer suggested would potentially strengthen this work if supplemented. However, as aforementioned, in our humble opinion, we think that the experiments that the reviewer suggested are either outside the scope of this paper or have no significant benefits over the experiments that were already conducted, and hence are not essential to the present study.

References

1. Nichols, R. and I.A. Lim, Spatial and temporal immunocytochemical analysis of drosulfakinin (Dsk) gene products in the Drosophila melanogaster central nervous system. Cell Tissue Res, 1996. 283(1): p. 107-16.

2. Marder, E., et al., Distribution and partial characterization of FMRFamide-like peptides in the stomatogastric nervous systems of the rock crab, Cancer borealis, and the spiny lobster, Panulirus interruptus. J Comp Neurol, 1987. 259(1): p. 150-63.

3. Nassel, D.R. and M.J. Williams, Cholecystokinin-like peptide (DSK) in Drosophila, not only for satiety signaling. Front Endocrinol, 2014. 5.

4. Hwang, R.Y., et al., Nociceptive neurons protect Drosophila larvae from parasitoid wasps. Curr Biol, 2007. 17(24): p. 2105-2116.

5. Tracey, W.D., Jr., et al., painless, a Drosophila gene essential for nociception. Cell, 2003. 113(2): p. 261-73.

6. Xiang, Y., et al., Light-avoidance-mediating photoreceptors tile the Drosophila larval body wall. Nature, 2010. 468(7326): p. 921-6.

7. Burgos, A., et al., Nociceptive interneurons control modular motor pathways to promote escape behavior in Drosophila. eLife, 2018. 7.

8. Honjo, K. and W.D. Tracey, Jr., BMP signaling downstream of the Highwire E3 ligase sensitizes nociceptors. PLoS Genet, 2018. 14(7): p. e1007464.

9. Im, S.H., et al., Tachykinin acts upstream of autocrine Hedgehog signaling during nociceptive sensitization in Drosophila. eLife, 2015. 4: p. e10735.

10. Ohyama, T., et al., A multilevel multimodal circuit enhances action selection in Drosophila. Nature, 2015. 520(7549): p. 633-9.

11. Honjo, K., R.Y. Hwang, and W.D. Tracey, Jr., Optogenetic manipulation of neural circuits and behavior in Drosophila larvae. Nat Protoc, 2012. 7(8): p. 1470-8.

12. Zhong, L., et al., Thermosensory and non-thermosensory isoforms of Drosophila melanogaster TRPA1 reveal heat sensor domains of a thermoTRP channel. Cell Rep, 2012. 1(1): p. 43-55.

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Reply to the reviewers

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

Major points:

1. Although the role of mitofusin on mitochondrial morphology has been established by others and comprehensively assessed in the present study, the authors should determine the functional outcome from the genetic manipulations on Mfn2 and Mfn1. As observed by increased glucose uptake, one could hypothesize an impairment in mitochondrial oxidative phosphorylation, leading the cells to rely uniquely or heavily on glycolysis as a fuel. Also, as mentioned by the authors in the discussion, ROS play a fundamental role in adipogenesis, and, therefore, mitochondrial ROS emission and/or cellular redox balance should also be assessed. I believe these two experiments will add insightful information to the current dataset.

__Thank you for these suggestions. Whilst we agree with the general premise of this point, unfortunately quantifying oxidative phosphorylation and ROS production with sufficient precision to detect relatively subtle changes remains very challenging. We have attempted these experiments but they require considerable optimisation (particularly using adipocytes). Preliminary studies done in MEFs (Cover letter figure 1) suggest that under some stimuli there may be higher ROS in Mfn1 and Mfn2 knock-out lines. However this preliminary data would require further optimisation and repetition in adipocytes, which is more challenging. __

For now, we have amended the Discussion to specify that these experiments are of particular interest.

Cover letter figure 1. Levels of reactive oxygen species (ROS) in mouse embryonic fibroblasts measured by flow cytometry for fluorometric dyes CellROX (total cellular ROS), D2-HDCFA (total cellular ROS), and MitoSOX (mitochondrial ROS). Levels are expressed relative to wild-type. MEFs were treated with antimycin A (or media only) for 20minutes prior to incubation with the ROS dyes, then washed three times before assayed. AntA, Antimycin; CR, CellROX; M1, Mfn1-/- MEFs; M2, Mfn2-/- MEFs; MS, MitoSOX; WT, wild-type.

The insulin effect on glucose uptake does not allow to conclude any impairment in insulin responsivity. The fold change of glucose uptake mediated by insulin was roughly 1.2 in undifferentiated adipocytes, 2.3 in differentiated WT, and 2.5 in Mfn1KO differentiated adipocytes. The absolute increase in glucose uptake could be a compensatory mechanism due to impairment in mitochondrial bioenergetics (see point #1), given that the cells can still respond to insulin. Measuring Akt phosphorylation levels following insulin treatment would help solve this issue.

__As requested, we have assessed the effect of insulin treatment on Ser 473 phosphorylation of Akt2 (Pkb) in wild-type and knock-out MEFs differentiated into adipocytes (Fig 2D). Mfn1_-/-_ MEFs show an increase in Akt phosphorylation relative to the other cell lines. They also have higher expression of insulin receptor and Glut4, consistent with their degree of adipogenic differentiation. __

We agree that impaired mitochondrial bioenergetics could account for the observations in perturbed glucose uptake in the knockout cell lines (especially Mfn2-null) and have therefore amended the text throughout to reflect this.

Usually, working with clonal transgenic cells lines has the limitations that the cells might behave differently in terms of adipogenic potential over passages. A transient loss of function in the same cells would solve this concern. Also, introducing the patient mutations might be closer to the human situation than working with KO mouse fibroblasts.

__We agree with this potential concern, which is why we conducted knock-down studies in 3T3-L1 cells in addition to the work in knockout MEFs. These data were concordant with what we observed in the KO MEFs so we don’t think it is necessary to conduct repeat KD experiments in WT MEFs. __

In our previous study we observed that human fibroblasts with biallelic MFN2-R707W mutations did not have any obvious phenotype (____https://elifesciences.org/articles/23813____). We have separate work studying these mutations in vivo where we provide further characterisation of murine adipocytes harbouring Mfn2-R707W; this work is now published here: https://elifesciences.org/articles/82283

Minor points:

1. Although the authors mention in the introduction that the differentiation of adipocytes is followed by an increase in mitochondrial mass, it would be interesting the determine the expression profile of mfn1 and mfn2 during the differentiation process.

We have found that there is an increase in markers of mitochondrial fusion (Mfn1 & Mfn2) as well as fission (Fis1) throughout differentiation of 3T3-L1s. ____We have included this data in the manuscript (Supplementary Figure ____6A ).

The authors should discuss other models, even though pre-clinical, of mitochondrial dysfunction that results in lipodystrophy but with different metabolic outcomes. To cite a few but not only PMID: 29588285; PMID: 21368114; PMID: 31925461.

Thank you for this suggestion. We have added a section on this in the introduction.

It would be interesting to discuss the role of Mfn1/2 in the context of cold-induced adipogenesis, given the prominent role of mitochondrial dynamics, as mentioned by the authors in the reference list, on cold-induced adaptative thermogenesis (Mahdaviane et al. 2017; Boutant et al. 2017).

Thank you for this suggestion. We have added a section on this in the introduction.

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

• In Fig.2A, the authors report "increased lipid accumulation in Mfn1-/- MEFs, but not in Mfn2-/- MEFs". While the overall content might be similar, the pattern of lipid accumulation seems to be different. Indeed, differences in lipid droplet morphology have been observed in Mfn2 KO MEFs upon oleate treatment (McFie et al., 2016). The manuscript would benefit from having quantifications of lipid droplet size and number.

Thank you for highlighting this. We have quantified lipid droplet size and, consistent with McFie et al have found increased size in Mfn2 knock-down. This data is now included in Supplementary Figure 6B.

• Following the above point, McFie et al. also reported that Mfn1/Mfn2 double KO MEFs could differentiate into adipocytes. The authors should discuss these opposing observations. The contrasting observation may be due to acquired clonal differences in MEF lines. We have attempted ‘double’ knock down (of both Mfn1 and Mfn2 concurrently) in 3T3-L1 cells however this was essentially lethal and also did not generate any cells capable of differentiation. We have added a section in the Discussion regarding this point.

• In relation to the effects of Mitofusin deletions on glucose uptake, the authors mention that Mfn2 KO MEFs show impaired insulin stimulated glucose uptake. The interpretation of the result is not straight forward, as basal glucose uptake is highly increased in Mfn2 KO MEFs. Maybe there is simply a treshold for maximal glucose uptake capacity in MEF-derived adipocytes. In any of these cases, the authors might want to check GLUT1 levels, in line of their suggestion that the increased basal glucose uptake might be related to higher GLUT1. Alternatively, the authors might also want to check elements of the insulin signaling path, in case there are alterations that could explain the phenomenon.

As mentioned above in response to reviewer 1, we have now ____performed immunoblots to quantify some components of the insulin signalling cascade (Fig 2D). We observed lower expression of both Glut1 and Glut4 in the Mfn2-/- cells. Mfn2-/- cells did demonstrate some Akt phosphorylation but considerably less than Mfn1-/- cells. These results are now included in the revised manuscript (Figure 2D).

• In line with the above point, one would have wished that mitochondrial biology was better characterized in the different MEF models. While mitochondrial shape analyses are provided, some information on, at least, mitochondrial respiratory capacity, glucose oxidation and/or fatty acid oxidation rates, would be important. This would allow for a more solid discussion on why Mfn2 KO MEFs display such high basal glucose uptake rates.

We have responded to a similar suggestion from Reviewer 1, above.

• In relation to the experiments in MEFs, one should never forget that WT, Mfn1 and Mfn2 KO MEFs derive from different mice. Hence, the phenotypes could be related to trait variabilities in the origin mice themselves, and not just the gene deletion. To control for this aspect, the authors could simply re-introduced Mfn1 or Mfn2 in their respective MEFs and evaluate if their alterations are normalized.

__Yes one could try this but we have addressed this general concern by replicating the impact of Mfn1/2 KD in 3T3L1 cells so are not inclined to pursue this at this time. __

• Transcriptomic analyses reveals a decrease in adipogenic gene expression in Mfn2 KO MEFs. However, lipid accumulation is comparable to WT MEFs is normal. This could be due to defects in lipolytic capacity, leading to similar lipid accumulation despite lower adipogenic capacity. This could be tested by evaluating the adrenergic response of these cells (e.g.: glycerol release).

Thank you for this suggestion. We have commented in the Discussion to explain that we have not fully characterised this mechanism.

• The experiments in 3T3-L1 would also benefit from some gene expression analyses to evaluate if Mfn1 depletion leads to acceleration and/or magnification of the differentiation stages. In relation to this, 3T3-L1 cells could be used to monitor Mfn1 and Mfn2 through differentiation, which in itself would be valuable information.

We have performed a protein-level time course for markers of mitochondrial fusion (Mfn1 & Mfn2) as well as fission (Fis1) throughout differentiation of 3T3-L1s. We have included this data in the manuscript (Supplementary Figure 6A). We think that changes in protein expression are more relevant than changes in mRNA so have not included gene expression changes at this time.

CROSS-CONSULTATION COMMENTS The comments from the three independent reviewers are extremely well aligned and agree that improving the following aspects could largely benefit the manuscript:

• A better metabolic characterisation of the models used
• Provide measurements in relation to mitochondrial bioenergetics and ROS production – we have attempted this but the data is not very clear in our view and warrants further optimisation which we are not inclined to pursue currently. - Explorations of insulin signaling - done thank-you.
• Improve the validation and significance of the cellular models used, following the different suggestions from the three reviewers. Most notably, considering the introduction of human Mfn2 mutation forms – we have published a separate manuscript on follow up work on the human MFN2 variant as mentioned above.

A number of additional comments are raised, all of which are very reasonable and, in my opinion, should not be difficult to address. I think we can all agree that a mechanistic underpinning of the observations would give a larger degree of novelty to the work. Also, none of us would like the revision's quality to be constraint by a tight deadline. I would therefore be totally OK to extend the timeframe for the revision beyond the original 3 months proposed.

Reviewer #2 (Significance (Required)):

This is an interesting and well-crafted manuscript. Mice deficient for Mfn2 or Mfn1 have been reported by different laboratories, yet most of them fail to explore the effects on early adipogenesis. The study is limited to cultured cells, but this is well acknowledged by the authors Given the existence of human mutations in the mitofusin-2 gene that largely alter fat mass distribution, this work provides new clues on how these mutations might impact adipose tissue.

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

Mann et al. The objective of this study is to determine the extent to which mitofusins (Mfn1 and Mfn2) have redundant functions and assess their contributions to adipocyte differentiation. While a point mutation in the Mfn2 gene has been associated with severe adipose tissue dysfunction and lipodystrophy, no disease phenotypes have been linked to mutations in Mfn1. To address these objectives, the authors sought to characterize how adipocyte differentiation and function is affected in Mfn1, Mfn2 or double knockout adipocytes in two distinct in vitro models. Their findings indicate divergent effects of Mfn1 and Mfn2 on adipocyte differentiation and function despite similar alterations to mitochondrial morphology. Loss of Mfn1 promotes adipogenesis while Mfn2 decreases it. The authors conclude that these findings are indicative of non-redundant functions in Mfn1 and Mfn2.

Major comments: The observation that Mfn1 KO/KD leads to increased adipogenesis in vitro is somehow novel and, perhaps, surprising, as the author say. However, the molecular understanding underlying this phenotype remains unexplored. The analyses performed are mainly descriptive and don't dig deeper into the identification of the molecular mechanism. They do hypothesize that ROS production may be responsible for the observed effects, but that's how far they go.

The authors do highlight the limitations of this work, but these limitations need careful consideration, for not addressing them seriously limits the novelty of this study, especially not testing these conditions in human cells. The current version of this work seems too preliminary to suggest useful experiments that could strengthen the study, since future analyses could take many different directions.

Yes, we accept that the findings are rather preliminary but our initial efforts suggest that precisely elucidating the underlying mechanism/s is likely to be more difficult and complicated than alluded to by the reviewers. We would therefor prefer to share our initial observations so that others can also attempt to clarify the underlying mechanisms.

A few unanswered questions that the authors might consider are: What is the difference between the Arg707Trp mutation and the KO/KD? Mfn1 and 2 deletions lead to fragmented mitochondria, but opposite adipogenic potentials. What other mitochondrial defects can explain it? Are organelle contact site disrupted only with Mfn2? How does Mfn1 and 2 KO/KD affect mitochondrial proteome? What does mitochondrial bioenergetics look like? How is ROS production affected? Is the increased glucose uptake (basal) a compensatory mechanism for mitochondrial dysfunction? Thank you for these suggestions. We acknowledge that this work is largely descriptive in nature. These are all questions that should be addressed to improve mechanistic understanding of our observations.

__The difference between p.Arg707Trp and KO/KD is challenging to address because in the non-adipose cell lines studied so far (human and mouse fibroblasts) there has been no evidence of perturbation of the mitochondrial network. __

As discussed above, we have done preliminary studies into ROS production but are unable to provide a complete characterisation at this time. Similarly, we have not been able to perform bioenergetic studies (e.g. Seahorse, Oxyboros) that would provide more insight into differences between Mfn1 and Mfn2 KO cell lines.

CROSS-CONSULTATION COMMENTS I agree the work is interesting, but is too preliminary and merely descriptive. the experiments suggested will significantly improve the manuscript. However, I don't think they will take only three months to be completed. This work needs a significant amount of work including the study of the mechanism, at least an idea of what the mechanism could be, to be considered novel.

We accept this limitation and have responded to this general point above.

Reviewer #3 (Significance (Required)):

Understanding how mitochondrial dynamics affect adipogenic differentiation is critical to better understand how metabolism impact cell signaling, cell fate and function.

Strengths: this work reveals an interesting phenotype for Mfn1 and Mfn2 mutant preadipocytes. Weaknesses: this work is merely descriptive and preliminary to provide a clear understanding of the observed phenotypes

Advance: Although the performed experiments are accurate, well designed, and well controlled, the fact that Mfn1 and 2 have distinct functions and cannot compensate for one another was already clear based on the embryonic lethality of either Mfn1 and Mfn2 KO mice as well as the Mfn2 mutation in humans that leads to a pathological condition.In the current verison, this work minimally contributes to advancing the field.

Audience: an extensively revised version of this work including deeper phenotyping of thier models and human cell work would be of interest for sceintists studying mitchondrial biology, adipose tissue, metabolic diseases, and human genetic diseases.

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

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Reply to the reviewers

Reply to reviewers.

We deeply thank the reviewers for the time spent on evaluating our manuscript as well as providing comments and suggestions to improve our study.

__Reviewer #1 (Evidence, reproducibility and clarity (Required)): __

*In this manuscript Lebdy et al. describe a new role of GNL3 in DNA replication. They show that GNL3 controls replication fork stability in response to replication stress and they propose this is due to the regulation of ORC2 and the licensing of origins of replication. Their data suggest that GNL3 regulates the sub nuclear localization of ORC2 to limit the number of licensed origins of replication and to prevent resection of DNA at stalled forks in the presence of replication stress.

While many of the points of the manuscript are proven and well supported by the results, there are some experiments that could improve the quality and impact of the manuscript. The main issue is that the connection between the role of GNL3 in controlling ORC2, the firing of new origins and the protection of replication forks is not clearly established. At the moment the model relies on mainly correlative data. In order to further substantiate the model, we propose to address some of the following issues:*

1. *The authors indicate that RPA and RAD51 accumulation at stalled forks is not affected by GNL3 depletion. These data should be included and other proteins should be analysed. In addition, the role of helicases could be explored through the depletion of the main helicases involved in the remodelling of the forks. * Response: As asked by the reviewer we will add the fractionation experiments that show that the level of RAD51 and RPA on chromatin is not affected by GNL3 depletion. So far, the other proteins we checked (RIF1 and BRCA1), both involved in nascent strand protection, did not show clear differences. Therefore, we concluded that depletion of GNL3 does not seem to affect the recruitment of major proteins required for protection of nascent DNA. Of course, we cannot exclude that other proteins may be affected by GNL3 depletion, but testing all the possible candidates would be time consuming with a very low chance of success. In addition, fractionation experiments are possibly not quantitative enough to uncover small differences and may be not that informative. Thus it remains possible that RPA exhaustion may be the cause of resection in absence of GNL3 as suggested by the work conducted in Lukas’ lab (Toledo et al. 2013. https://pubmed.ncbi.nlm.nih.gov/24267891/). To test this hypothesis, we will analyze if resection in absence of GNL3 is still occurring in a well-characterized cell line that overexpress the three RPA subunits that we obtained from Lukas’ lab.

To our knowledge not many helicases have been shown to be involved in remodeling of stalled forks. The best example is RECQ1, however we feel that testing RECQ1 involvement in resection upon GNL3 depletion will complicate our story without adding much regarding the mechanism. We hope the reviewer understands our concern.

• The proposed model implies that GNL3 depletion leads to increased origin licensing. FThe authors should address if the primary effect of GNL3 depletion is on origin firing by using CDC7 inhibition in the absence of stress (Rodríguez-Acebes et al., JBC 2018). *

__Response: __This is an excellent point raised by the reviewer. To test if the primary effect of GNL3 depletion in on origin firing we will test if the defect in replication fork progression is dependent on CDC7 using DNA fibers experiments and CDC7 inhibitor.

• A way to prove that origin firing mediates the effect of GNL3 on fork protection would be to reduce the number of available origins. The depletion of MCM complexes has been shown to limit the number of back-up origins that are licensed and leads to sensitivity to replication stress (Ibarra et al., PNAS 2008). If GNL3 depletion results in increased number of origins, this effect should be prevented by the partial depletion of MCM complexes. *

__Response: __This is also an excellent point. We will test if MCM depletion decreases resection upon GNL3 depletion and treatment with HU. In addition, we will integrate in the manuscript experiments that we have done recently that show that treatment with roscovitine, a CDK inhibitor that impairs origin firing, decreases the level of resection observed in absence of GNL3. We think this experiment strengthens the results obtained with CDC7 inhibitors.

*Alternatively, the authors could try to modulate the depletion of GNL3. Origin licensing takes place in the G1 phase and thus the depletion of GNL3 by siRNA could affect the following S phase. Using an inducible degron for GNL3 depletion would allow to deplete GNL3 in G1 or S phase specifically. If the model is correct, the removal of GNL3 in S phase should not affect fork protection but removing GNL3 in the previous G2/M phase should reduce the number of licensed origins and lead to impaired fork protection. *

__Response: __This is obviously a good point given the fact that GNL3 deletion is not viable (see responses to reviewer 2). We tried to develop an auxin induced degron of GNL3, but we could not obtain homozygous clones, meaning that our clones had always an untagged GNL3 allele. Since GNL3 is essential its tagging may impair its function, explaining why we could not obtain homozygous clones. However, we are planning to optimize the design using other degrons system (for instance Halo-tag) to address the role of GNL3 specifically during S-phase. But we think this is above the scope of the present study.

*In addition to the connection GNL3-origin firing-fork protection, it is unclear how the lack of GNL3 in the nucleolus and the change in the sub nuclear localization of ORC2 controls origin firing and resection. The strong interaction observed between GNL3-dB and ORC2, and the subsequent change in ORC2 localization does not explain how origin licensing can be affected. In this sense, the authors could address: *

1. *Does the depletion of GNL3 and the expression of GNL3-dB affect the formation of the ORC complex, its subnuclear localization or its binding to chromatin? The authors have not explored if the interaction of GNL3 with ORC2 is established in the context of the ORC complex. An IF showing NOP1 with PLA data from GNL3-dB and ORC2 is needed to analyse how the expression of increasing amounts of GNL3-dB affects ORC2. * __Response: __We tested if GNL3 depletion impacts ORC2 and ORC1 recruitment on chromatin, but we could not observe significant differences. No clear differences were observed upon GNL3-dB expression either. One reason for this may be due to the excess of ORC complex on the chromatin, in addition chromatin fractionation is likely not sensitive enough to observe small differences. We think that quantitative ChIP-seq of ORC2 or other ORC subunits upon GNL3 depletion is required to visualize such differences, but this is above the scope of the study, and this constitutes the following of this project. We also tried to look at subnuclear localization of ORC2 using immunofluorescence, but the signal was not specific enough to observe differences. We think that the increased interaction (PLA) of ORC2 with GNL3-dB (Figure 5E) demonstrates a change in ORC2 subnuclear localization. To confirm this, we will perform the excellent experiment proposed by the reviewer to test if increasing level of GNL3-dB affects its interaction with ORC2 using PLA.

We do not think that the interaction between ORC2 and GNL3 is established in the context of the ORC complex since only ORC2 (and not the other ORC) was significantly enriched in the GNL3 Bio-ID experiment. The full list of proteins from the Bio-ID experiment (Figure 4A) will be provided in the revised version. Therefore, we think that either GNL3 regulates ORC2 subnuclear localization that in turns impact the ORC complex or GNL3 regulates ORC2-specific functions. More and more evidences show that ORC2 plays roles possibly independently of the ORC complex (see Huang et al. 2016 https://doi.org/10.1016/j.celrep.2016.02.091 or Richards et al. 2022 https://doi.org/10.1016/j.celrep.2022.111590 for instance). Future work should uncover how these ORC2 functions may regulate origins activity.

*In order to confirm if the mislocalization of ORC2 by the expression of GNL3-dB increases origin firing and mediates the effects on fork protection the authors could check DNA resection levels inhibiting CDC7 in high GNL3-dB conditions. Also, the levels of MCM2, phosphor-MCM2, CDC45, have not been analysed upon expression of GNL3-dB. *

__Response: __This is a good point; we will test if the resection observed upon expression of GNL3-dB is dependent on origin firing using CDC7 inhibitor. We have not measured the level of the cited proteins but instead we performed DNA combing to measure Global Instant Fork Density. We now show that expression of GNL3-WT suppresses the increased origin firing observed upon GNL3 depletion, in contrast expression of GNL3-dB does not suppress it. This important result indicates that origin firing is increased upon GNL3-dB expression, providing a link between aberrant localization and increased firing. These data will be part of the revised version of the manuscript.

The data in the paper suggest that GNL3 may affect the role of ORC2 in centromeres. Since depletion of GNL3 leads to increased levels of gH2AX, it would be interesting to address if this damage is due to incomplete replication in centromeres by analysing the co-localization of g*H2AX and centromeric markers both in unstressed conditions and upon the induction of replication stress. *

__Response: __This is indeed and interesting comment, however since it has been previously shown that gH2AX signal is rather strong upon GNL3 depletion (see Lin et al. 2013. https://pubmed.ncbi.nlm.nih.gov/24610951/ ; Meng et al. 2013. https://pubmed.ncbi.nlm.nih.gov/23798389/) we do not think that co-localization experiments with CENP-A for instance will be informative given the high number of gH2AX foci.

*Minor points: *

1. In the initial esiRNA screen the basal levels of g*H2AX should also be shown. * Response: Our negative control is the transfection of an esiRNAs that targets EGFP (a gene that is not expressed in the tested cell line). This esiRNAs is ranked at the end of the list and therefore constitutes the basal level of gH2AX signal. In any case it is well-established that GNL3 depletion increases gH2AX signal (see Lin et al. 2013. https://pubmed.ncbi.nlm.nih.gov/24610951/ ; Meng et al. 2013. https://pubmed.ncbi.nlm.nih.gov/23798389/).

*Figure EV1B: I think the rank needs another RS mark to see better the effect of each esiRNA on DNA lesions (high variability in all the conditions showed). *

__Response: __We understand this issue, but we cannot repeat this set of experiments for technical reasons (reagents and cost mainly). Anyway, we believe that the role of GNL3 is response to replication stress is extensively addressed by other experiments of this manuscript.

*Figure 1C and Figure EV1D/E: the quantification of the pCHK1/CHK1 levels could be included to show that there are no changes in phosphorylation upon GNL3 depletion. *

Response: it is a good point; we will put quantification in the revised version.

*In the first section of the results, at the end Figure 4B is incorrectly called for. *

__Response: __Thanks for the comment, we will modify accordingly.

The levels of GLN3 expression in 293 cells should be already included in section GNL3 interacts with ORC2.

__Response: __We will add a figure that shows the level of expression in 293 cells.

The full MS data needs to be included for both GNL3 and ORC2.

__Response: __This will be integrated in the revised version.

Figure 4B should be improved, since there is a faint band in the IgG mouse control.

__Response: __it is true that the figure is not perfect, but we believed that our Bio-ID and PLA experiments fully demonstrate the interaction between GNL3 and ORC2.

__Reviewer #1 (Significance (Required)): __

*The work is nicely written, the figures are well presented and the experiments have the necessary controls. It provides relevant information to understand how replication stress is controlled and linked to replication fork protection through origin firing. These results are relevant to the field, linking GNL3 to origin firing and with potential to help understand the role of GNL3 in cancer. They provide new information and can give rise to new studies in the future. Many of the conclusions of the manuscript are well supported. Additional support for some of the main claims would strengthen the results and also increase the impact providing a bigger conceptual advance by performing some of the suggested experiments. *

__Reviewer #2 (Evidence, reproducibility and clarity (Required)): __

*This manuscript explores the role of GNL3/nucleostemin in DNA replication and specifically in the response of DNA replication to DNA damage. GNL3 is a predominantly nucleolar protein, previously characterised as a GTP-binding protein and shown to be necessary for effective recruitment of the RAD51 recombinase to DNA breaks. The entry point for this report is a mini screen, based on proteins identified previously by the authors to associate with replication forks by iPOND, for factors that increase gamma-H2Ax (an indicator of DNA damage) after treatment with the Top1 inhibitor camptothecin (CPT). In this mini-screen GNL3 emerged as the top hit.

The authors put forward the hypothesis that GNL3 is able to sequester the replication licensing factor ORC2 in the nucleolus and that failure of this mechanism leads to excessive origin firing and DNA resection following CPT treatment.*

• The model put forward is interesting, but currently rather confusing. However, for the reasons upon which I expand below, I do not believe that the data provide a compelling mechanistic explanation for the effects that are reported and I am left not being certain about some of the links that are made between the various parts of the study, even though individual observations appear to be of good quality. *

*Specific points: *

*The knockdown of GNL3 is very incomplete. In this regard, the complementation experiments are welcome and important. However, is it an essential protein? Can it be simply deleted with CRISPR-Cas9?

*__Response: __There are obviously variations between experiments but overall, the depletion of GNL3 using siRNA seems good in our opinion. Deletion of GNL3/nucleostemin leads to embryonic lethality in mouse (Beekman et al. 2006. https://pubmed.ncbi.nlm.nih.gov/17000755/ ; Zhu et al. 2006. https://pubmed.ncbi.nlm.nih.gov/17000763/). ES cells deleted for GNL3 can be obtain but do not proliferate probably because of their inability to enter in S-phase (Beekman et al. 2006. https://pubmed.ncbi.nlm.nih.gov/17000755/). We wanted to test if it was the case in our cellular model and we tried to delete it using CRISPR-Cas9. We managed to obtain few clones deleted for GNL3, but they grow really poorly prevented us to do experiments. To bypass this, and as suggested by the reviewer 1, we tried to make an auxin-induced degron of GNL3. Unfortunately, we did not manage to obtain homozygous clones, only heterozygous. One possibility could be that the tagging induced a partial loss of function of GNL3, and since GNL3 is essential, it may explain why we did not obtain homozygous clones. We may also want to use alternative degron systems such as Halo-Tag, but we believe this is out of the scope of the study.

__ __*Global instant fork density is not quite the same as actually measuring origin firing. Ideally, it would be good to see some more direct evidence of addition origin firing e.g. by EdU-seq (Macheret & Halazonetis Nature 2018) but this would be quite a significant additional undertaking. However, given the authors have performed DNA combing with DNA counterstain, they should be able to provide accurate measurements of origin density and inter-origin distance. *

__Response: __As indicated by the reviewer EdU-seq would need a lot of development since we are not using this approach in our team. In addition, this method can detect replication origins only if performed in the beginning of S-phase, meaning that only the early firing origins will be detected and not the others. GIFD measurement is actually directly linked with origin firing since it is counting the forks to duplicate the genome. The measurements of IODs have at least two main limitations: (1) there is a bias for short IODs due to the length of analyzed fibers and (2) it focuses only on origins within a cluster not globally. Overall, we believe that GIFD is the method of choice to measures origins firing. In addition, these experiments have been done by the lab of Etienne Schwob (see acknowledgments), a leader in the field.

*'Replication stress' is induced with CPT. This term is frequently used to describe events that lead to helicase-polymerase uncoupling (e.g. O'Connor Mol Cell 2015) but that is not the case with CPT, which causes fork collapse and breaks. Are similar effects seen with e.g. UV or cisplatin? Additionally, a clear statement of the authors definition of replication stress would be welcome. *

__Response: __We will better define the term ‘replication stress’ in the revised version of the manuscript. It should be understood, in our case, that any impediment that leads to replication fork stalling and measurable by DNA combing or Chk1 phosphorylation. We have not performed experiments using UV and cisplatin.

*It is really not clear how the authors explain the link between potential changes in origin firing and resection. i.e. What is the relationship between global origin firing and resection at a particular fork, presumably broken by encounter with a CPT-arrested TOP1 complex. What is the link mechanistically? This link needs elaborating experimentally or clearly explaining based on prior literature. *

• *__Response: __Most of our results on resection has been performed with hydroxyurea, but it is true that we saw resection in absence of GNL3 in response to CPT. Treatment with HU or CPT reduces fork speed and activates additional replication origins (see Ge et al. 2007 https://pubmed.ncbi.nlm.nih.gov/18079179/ for HU or Hayakawa et al. 2021 https://pubmed.ncbi.nlm.nih.gov/34818230/ for CPT ). When GNL3 is depleted, more forks are active, meaning more targets for HU and CPT. In addition, it is likely that the firing of additional origins in response to HU and CPT is stronger in absence of GNL3. Because of this we believe that factors required to protect stalled forks may be exhausted explaining why resection is observed. This is inspired by the work of Lukas’ lab (Toledo et al. 2013 https://pubmed.ncbi.nlm.nih.gov/24267891/) and is described in the figure 6. One obvious candidate that may be exhausted is RPA, to test this we will check if resection upon GNL3 depletion and treatment with HU is still occurring in cell lines provided by Lukas’ lab that overexpress RPA complex (described in Toledo et al.). We will explain our model more carefully in the revised version.

*Related to this, I remain unconvinced that the experiments in Figure 3 show that the effects of ATRi and Wee1i on origin firing and on resection are contingent on each other. I do not believe that the authors have adequately supported the statement (end of pg 9) 'We conclude that the enhanced resection observed upon GNL3 depletion is a consequence of increased origin firing.' The link between origin firing and resection needs really needs further substantiation and / or explanation.

*__Response: __Our rational was the following. Inhibition of ATR or WEE1 increase replication origin firing, a situation that may be like the one observed for GNL3 depletion. In Toledo et al, they show that inhibition of WEE1 or ATR induces exhaustion of RPA. This exhaustion is reduced in presence of CDC7 inhibitor, roscovitine (a CDK inhibitor that inhibits origin firing) or depletion of CDC45, indicating that this is due to excessive origin activation. In our case we show that the resection observed upon WEE1 or ATR inhibition is reduced upon treatment with CDC7 inhibitor. We conclude that excessive replication origin firing induces DNA resection. Since we observed the same thing upon GNL3 depletion (but not upon BRCA1 depletion) we conclude that excessive origin firing favors DNA resection likely through exhaustion of RPA. As indicated above we will test this hypothesis by overexpressing RPA. In addition, we now show that treatment with roscovitine decreases resection upon GNL3 depletion (this will be part of the revised manuscript), an experiment that we believe confirms that excessive replication origins firing is responsible for resection upon GNL3 depletion. As suggested by reviewer 1, we will also test if depletion of MCM also reduces resection observed in absence of GNL3.

*It is not clear whether the binding of ORC2 to GNL3 also sequesters other components of the origin recognition complex? Does loss of the ability of GNL3 to bind ORC2 actually lead to more ORC bound to chromatin? How does GNL3 contribute to regulation of origin firing under normal conditions? Is it a quantitatively significant sink for ORC2 and what regulates ORC2 release? *

Response: The results of GNL3 Bio-ID were extremely clear, we could not significantly detect any other ORC subunits than ORC2 (these data were not present in the manuscript but will be added in the revised version), therefore we believe that GNL3 may sequester/regulate only ORC2. We tried to see if GNL3 depletion was changing the binding of ORC1 and ORC2 to the chromatin, but we could not see any difference, one possibility may be that small differences are not detectable by chromatin fractionation. We believe that ChIP-seq or ORC2 or other ORC subunits in absence of GNL3 is required but this it out of the scope of the study. GNL3 may regulates the stability of the ORC complex on chromatin via ORC2 but GNL3 may also regulates other ORC2 functions, at centromeres for instance. It has been shown indeed that ORC2 plays roles possibly independently of the ORC complex (see Huang et al. 2016 https://doi.org/10.1016/j.celrep.2016.02.091 or Richards et al. 2022 https://doi.org/10.1016/j.celrep.2022.111590 for instance). How exactly this is affecting origin firing is still mysterious. This is something we are planning to address in the future.

We do not know if it is a quantitatively sink for ORC2 or how this is regulated, however we believe that the ability of GNL3 to accumulate in the nucleolus may sequester ORC2. Consistent with this, we show that a mutant of GNL3 (GNL3-dB) that diffuses in the nucleoplasm interacts more with ORC2 in the nucleoplasm suggesting a release. As suggested by reviewer 1 we will now test if the interaction between ORC2 and GNL3-dB is dependent on the level of expression of GNL3-dB. In addition, we now show that expression of GNL3-dB increases replication origin firing like GNL3 depletion (data that will be added in the revised version), suggesting that regulation of ORC2 is the major cause of increased firing upon GNL3 depletion.

*Minor points: *

*All blots should include size markers *

__Response: __We will add them

*Some use of language is not sufficiently precise. For instance: ** - the meaning of 'DNA lesions' at the end of the first paragraph of the introduction needs to be more explicit. *

* - the approach to measurement of these 'lesions' (monitoring gamma-H2Ax) needs to be spelled out explicitly, e.g. line 4 of the last paragraph of the introduction. *

*

• 'we observed that the interaction between GNL3-dB and ORC2 was stronger' ... I do not see how number of foci indicates necessarily the strength of an interaction. *

* - in many places throughout 'replication origins firing' should be 'replication origin firing' (or 'firing of replication origins'). *

__Response: __We will correct these language mistakes.

__Reviewer #2 (Significance (Required)): __

The model put forward here has the potential to shed light on an important facet of the cellular response to DNA damage, namely the control of origin firing in response to replication stress that will certainly be of interest to the DNA repair / replication community and possibly more widely. The roles of GNL3 are poorly understood and this study could improve this state of affairs. However, the gaps in the mechanism outlined above and somewhat confusing conclusions do limit the ability of the paper to achieve this at present.

__Reviewer #3 (Evidence, reproducibility and clarity (Required)): __

*In this study, Lebdy et al propose a new mechanism to regulate the resection of nascent DNA at stalled replication forks. The central element of this mechanism is nucleolar protein GNL3, whose downregulation with siRNA stimulates DNA resection in the presence of stress induced by HU (Figure 1). Resection depends on the activity of nucleases MRE11 and CtIP, and can be rescued by reintroducing exogenous GNL3 protein in the cells (Figure 1G). GNL3 downregulation decreases fork speed and increases origin activity, without any strong effect on replication timing (Figure 2). Inhibition of Dbf4-dependent kinase CDC7 (a known origin-activating factor) also restricts fork resection (Figure 3). GNL3 interacts with ORC2, one of the subunits of the origin recognition complex, preferentially in nucleolar structures (Figure 4). A mutant version of GNL3 (GNL3-dB) that is not sufficiently retained in the nucleoli fails to prevent fork resection as the WT protein (Figure 5). In the final model, the authors propose that GNL3 controls the levels of origin activity (and indirectly, stalled fork resection) by maintaining a fraction of ORC2 in the nucleoli (Figure 6). *

This model is interesting and provocative, but it also relies on a significant degree of speculation. The authors are not trying to "oversell" their observations, because the Discussion section entertains different interpretations and possibilities, and the model itself contains several interrogative statements (e.g. "ORC2-dependent?"; "exhaustion of factors?").

• While the article is honest about its own limitations, the major concern remains about its highly speculative nature. I have some questions and suggestions for the authors to consider that could contribute to test (and hopefully support) their model. *

• *If GNL3 downregulation induces an excess of licensed origins and mild replicative stress resulting in some G2/M accumulation (Figure 2), what is the consequence of longer-term GNL3 ablation? Do the cells adapt, or do they accumulate signs of chromosomal instability? (micronuclei, chromosome breaks and fusions, etc) * __Response: __This is an important point also raised by Reviewer 2: deletion of GNL3 leads to embryonic lethality in mouse and ES cells deleted for GNL3 do not proliferate and fail to enter into S-phase. Consistent with this, the clones deleted for GNL3 that we obtained using CRISPR-Cas9 grow poorly, thus preventing us to do experiments. To our knowledge micronuclei and chromosome breaks have never been analyzed upon transient depletion of GNL3 using siRNA. However, it is well established that depletion of GNL3 induces phosphorylation of H2A.X) and the formation of ATR, RPA32 and 53BP1 foci due to S-phase arrest (Lin et al. 2013. https://pubmed.ncbi.nlm.nih.gov/24610951/ ; Meng et al. 2013. https://pubmed.ncbi.nlm.nih.gov/23798389/). DNA lesions have also been visualized by comet assay (Lin et al. 2019. https://pubmed.ncbi.nlm.nih.gov/30692636/). Consistent with this we observed a weak increased of DNA double-strand breaks upon GNL3 depletion using pulse-field gel electrophoresis as well as mitotic DNA synthesis (MiDAS). We can integrate this data in the revised version of the manuscript if required. To sum up, it is clear that GNL3 depletion is inducing problems during S-phase that may lead to possible genomic rearrangements.

• The model relies on the link between origin activity and stalled fork resection that is almost exclusively based on the results obtained with CDC7i (Figure 3). But CDC7 has other targets besides pre-RC components at the origins, such as Exo1 (from the Weinreich lab, cited in the study), MERIT40 and PDS5B (from the Jallepalli lab, also cited). The effect of CDC7i could be exerted through these factors, which are linked to fork stability and DNA resection. The loss of BRCA1 (Figure 3F) could somehow entail the loss of control over these factors. Could the authors check the possible participation of these proteins?*

__Response: __It is true that CDC7 has other targets than pre-RC components. We therefore decided to inhibit origin firing using roscovitine, a broad CDK inhibitor, a strategy previously used in Lukas lab (Toledo et al. 2013. https://pubmed.ncbi.nlm.nih.gov/24267891/). We observed that treatment with roscovitine decreased significantly resection observed upon GNL3 depletion, confirming the link between origin activity and stalled fork resection. This will be integrated in the revised version of the manuscript. As asked by Reviewer 1, we will also perform depletion of MCM to strength our model.

Exo1 is indeed a target of CDC7 as shown by the Weinreich lab (Sasi et al. 2018. https://www.ncbi.nlm.nih.gov/pmc/articles/PMC6111017/) however the authors do not formally demonstrate that Exo1 phosphorylation is required for its activity. We observed that depletion of Exo1 significantly reduced resection upon GNL3 depletion (data that will be added in the revised version), indicating that the effect of CDC7 inhibitor could be exerted via the control of Exo1. This is why our BRCA1 control is important, it is well stablished that Exo1 is required for nascent strand degradation upon BRCA1 depletion (Lemaçon et al. 2017. https://www.ncbi.nlm.nih.gov/pmc/articles/PMC5643552/) but CDC7 inhibition has no effect on resection upon BRCA1 depletion suggesting that resection by Exo1 may not be regulated by CDC7 in our context.

As stated by the reviewer MERIT40 and PDS5B are targets of DDK kinases (Jones et al. 2021 https://doi-org.insb.bib.cnrs.fr/10.1016/j.molcel.2021.01.004) and seem to be required for protection of nascent DNA and in response to HU. However, little is known about the role(s) of these proteins and we think that adding them will complicate message. We hope the reviewer understands this.

The model also relies on the fact that GNL3-dB mutant (not retained in the nucleoli) is not sufficient to counteract fork resection induced by HU (Figure 5G). The authors should test directly whether GNL3-dB induces extra origin activation, using their available DNA fibers-based technique.

__Response: __This is an excellent point. We have now GIFD (Global Instant Fork Density) data that shows that the number of active forks is increased upon dB GNL3-dB expression. It demonstrates that when GNL3 is no longer retained in the nucleolus more origins are active. These data will be integrated in the revised version of the manuscript, and we believe further support the regulation of ORC2 by GNL3.

*Finally, the model implies an exquisite regulation of the amount of ORC2 protein, which could influence the number of active origins and the extent of fork resection in case of stress. In this scenario, one could predict that ORC2 ectopic expression would have similar, or even stronger effects, than GNL3 downregulation. Is this the case? *

__Response: __We completely agree with this prediction. However, we are afraid that overexpression of ORC2 may have indirect effects due to the many described functions of ORC2, therefore it may be difficult to interpret the data. We will give a try anyway.

*Even if the connection between origins and fork resection could be firmly established, the molecular link between them remains enigmatic. The authors hint (as "data not shown") that it is neither mediated by RPA nor RAD51. Unfortunately, the reader is left without a clear hypothesis about this point. *

__Response: __We will add data that show that RPA and RAD51 recruitment is not affected by GNL3 depletion. However, the sensitivity of chromatin fractionation approach may be too weak to detect low differences. Based on the work of Lukas Lab (Toledo et al. 2013 https://pubmed.ncbi.nlm.nih.gov/24267891/) one possible mechanism may be exhaustion of the pool of RPA. This may link the excessive activation of origins observed upon GNL3 depletion and resection. To test this, we will check if resection upon GNL3 depletion and treatment with HU is still occurring in cell lines that overexpress RPA complex (described in Toledo et al.) that we obtained from Lukas’ lab.

__ __ **Referees cross-commenting**

__ __In addition to each reviewer's more specific comments, the three reviews share a main criticism: the lack of mechanistic information about the proposed link between origin activity and resection of nascent DNA at stalled forks.

__Reviewer #3 (Significance (Required)): __

In principle, this study would appeal to the readership interested in fundamental mechanisms of DNA replication and the cellular responses to replicative stress.

For the reasons outlined in the previous section, I believe that in its current version the study is not strong enough to provide a new paradigm about origins being regulated by partial ORC2 sequestering at nucleoli. The other potentially interesting advance is the connection between frequency of origin activity and the extent of nascent DNA resection at stalled forks, but the molecular link between both remains unknown.

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From ELIMIMIAN 626: By saying "All art is quite useless," Wilde is not only using paradox or a rhetorical style, but enforces the concept that contraries do not imply a negation. By claiming "Vice and Virtue" form suitable "material for the artist," Wilde encourages us, as readers, to think that the realm of artistic discourse is limitless. Art enables us to view life clearly, but art, by itself, is incapable of any permanent rendering. Similarly, when we interpret art, we interpret life, since life's colors are enshrined in it. Thus, Wilde would argue Art and life are not contingent but may complement each other.

From WINWAR 171: This line struck right in the face of Victorian materialism and was coined indiscriminately; Its defenders interpreted it as an exaltation of art, but its opposers claimed it was dangerous to established values.

From DUGGAN 61: In this one sentence, Wilde encapsulates the complete principles of the Aesthetic Movement popular in Victorian England. That is to say, real art takes no part in molding the social or moral identities of society, nor should it. Art should be beautiful and pleasure its observer, but to imply further-reaching influence would be a mistake.

Reviewer #2 (Public Review):

The authors had two aims in this study. First, to develop a tool that lets them quantify the synaptic strength and sign of upstream neurons in a large network of cultured neurons. Second, they aimed at disentangling the contributions of excitatory and inhibitory inputs to spike generation.

For the quantification of synaptic currents, their methods allows them to quantify excitatory and inhibitory currents simultaneously, as the sign of the current is determined by the neuron identity in the high-density extracellular recording. They further made sure that their method works for nonstationary firing rates, and they did a simulation to characterize what kind of connections their analysis does not capture. They did not include the possibility of (dendritic) nonlinearities or gap junctions or any kind of homeostatic processes. I see a clear weakness in the way that they quantify their goodness of fit, as they only report the explained variance, while their data are quite nonstationary. It could help to partition the explained variance into frequency bands, to at least separate the effects of a bias in baseline, the (around 100 Hz) band of synaptic frequencies and whatever high-frequency observation noise there may be. Another weak point is their explanation of unexplained variance by potential activation of extrasynaptic receptors without providing evidence. Given that these cultures are not a tissue and diffusion should be really high, this idea could easily be tested by adding a tiny amount of glutamate to the culture media.

For the contributions of excitation and inhibition to neuronal spiking, the authors found a clear reduction of inhibitory inputs and increase of excitation associated with spiking when averaging across many spikes. And interestingly, the inhibition shows a reversal right after a spike and the timescale is faster during higher network activity. While these findings are great and provide further support that their method is working, they stop at this exciting point where I would really have liked to see more detail. A concern, of course is that the network bursts in cultures are quite stereotypical, and that might cause averages across many bursts to show strange behaviour. So what I am missing here is a reference or baseline or null hypothesis. How does it look when using inputs from neurons that are not connected? And then, it looks like the E/(E+I) curve has lots of peaks of similar amplitude (that could be quantified...), so why does the neuron spike where it does? If I would compare to the peak (of similar amplitude) right before or right after (as a reference) are there some systematic changes? Is maybe the inhibition merely defining some general scaffold where spikes can happen and the excitation causes the spike as spiking is more irregular?<br /> The averaged trace reveals a different timescale for high and low activity states. But does that reflect a superposition of EPSCs in a single trial or rather a different jittering of a single EPSC across trials? For answering this question, it would be good to know the variance (and whether/ how much it changes over time). Maybe not all spikes are preceded by a decrease in inhibition. Could you quantitify (correlate, scatterplot?) how exactly excitation and inhibition contributions relate for single postsynaptic spikes (or single postsynaptic non-spikes)? After all, this would be the kind of detail that requires the large amount of data that this study provides.

For the first part, the authors achieved their goal in developing a tool to study synaptic inputs driving subthreshold activity at the soma, and characterizing such connections. For the second part, they found an effect of EPSCs on firing, but they barely did any quantification of its relevance due to the lack of a reference.

With the availability of Neuropixels probes, there is certainly use for their tool in in vivo applications, and their statistical analysis provides a reference for future studies.<br /> The relevance of excitatory and inhibitory currents on spiking remains to be seen in an updated version of the manuscript.

I feel that specifically Figures 6 and 7 lack relevant detail and a consistent representation that would allow the reader to establish links between the different panels. The analysis shows very detailed examples, but then jumps into analyses that show population averages over averaged responses, losing or ignoring the variability across trials. In addition, while their results themselves pass a statistical test, it is crucial to establish some measure of how relevant these results are. For that, I would really want to know how much spiking would actually be restricted by the constraints that would be posed by these results, i.e. would this be reflected in tiny changes in spiking probabilities, or are there times when spiking probabilities are necessarily high, or do we see times when we would almost certainly get a spike, but neurons can fire during other times as well.<br /> I would agree that a detailed, quantitative analysis of this question is beyond the scope of this paper, but a qualitative analysis is feasible and should be done. In the following, I am detailing what I would consider necessary to be done about these two Figures:

Figure 6C is indeed great, though I don't see why the authors would characterize synchrony as low. When comparing with Figure 4B, I'd think that some of these values are quite high. And it wouldn't help me to imagine error bars in panel 6D.<br /> Figure 6B is useful, but could be done better: The autocovariance of a shotnoise process is a convolution of the autocovariance of underlying point process and the autocovariance of the EPSC kernel. So one would want to separate those to obtain a better temporal resolution. But a shotnoise process has well defined peaks, and the time of these local maxima can be estimated quite precisely. Now if I would do a peak triggered average instead of the full convolution, I would do half of the deconvolution and obtain a temporally asymmetric curve of what is expected to happen around an EPSC. Importantly, one could directly see expected excitation after inhibition or expected inhibition after excitation, and this visualization could be much better and more intuitively compared to panel 6E.<br /> Panel D needs some variability estimate (i.e. standard deviation or interquartile range or even a probability density) for those traces.<br /> Figure 6E: Please use more visible colors. A sensitivity analysis to see traces for 2E/(2E+I) and E/(E+2I) would be great.<br /> Figure 6F: with an updated panel B, we should be able to have a slope for average inhibition after excitation for each of these cells. A second panel / third column showing those slopes would be of interest. It would serve as a reference for what could be expected from E-I interactions alone.<br /> Figure 6G: Could the authors provide an interquartile range here?

Figure 7A: it may be hard to squeeze in variability estimates here, but the information on whether and how much variance might be explained is essential. Maybe add another panel to provide a variability estimate? The variability estimate in panel 7B and 7D only reflect variability across connections, and it would be useful to add panels for the timecourses of the variability of g (or E/(E+I) respectively).

As a suggestion for further analysis, though I am well aware that this is likely beyond the scope of this manuscript, I'd suggest the following analysis:<br /> I would split the data into the high and low activity states. Then I would compute the average of E/(E+I) values for spikes. Assuming that spikes tend to happen for local maxima of E/(E+I) I would find local maxima for periods without spike such that their average is equal to the value for actual spikes. Finally, I would test for a systematic difference in either excitation or inhibition.<br /> If there is no difference, you can make the claim that synaptic input does not guarantee a spike, and compare to a global average of E/(E+I).

Author Response

Reviewer #1 (Public Review):

First, we thank the reviewer for his instructive remarks. In the following we address the queries of Reviewer 1.

1.1) At several points, the authors make claims that I believe extend beyond the data presented here. For instance, in the Abstract (line 27), the authors state "the development of adult songs requires restructuring the entire HVC, including most HVC cell types, rather than altering only neuronal subpopulations or cellular components." The gene ontology analyses performed do suggest that there is a progression from cellular transcriptional changes to organ-level changes, however caution should be taken in claiming that "most HVC cell types" exhibit transcriptional changes. In fact, according to Fig. 3D most of the transcriptional changes appear restricted to neurons. As the authors themselves note elsewhere, claims at this resolution are difficult without support from single-cell approaches. I do not suggest that the authors need to perform single-cell RNA-seq for this work, but strong claims like this should be avoided.

We have revised our claim to more accurately reflect our findings. Our intended message is that testosterone treatment leads to extensive transcriptional changes in the HVC, likely affecting a majority of neuronal subpopulations rather than solely targeting specific cellular components. The revised text in lines 29-32 now reads: "Thus, the development of adult songs stimulated by testosterone results in widespread transcriptional changes in the HVC, potentially affecting a majority of neuronal subpopulations, rather than altering only specific cellular components."

1.2) Similarly the Abstract states that parallel regulation "directly" by androgen and estrogen receptors, as well as the transcription factor SP8, "lead" to the transcriptional and neural changes observed after testosterone treatment of females. However, experiments that demonstrate such a causal role have not been performed. The authors do perform a set of bioinformatic analyses that point in this direction - enrichment of androgen and estrogen receptor binding sites in the promoters of differentially expressed genes, high coexpression of SP8 with other genes, and the enrichment of predicted SP8 binding sites in coexpressed genes. However, further support for direct regulation, at the level that the authors claim, would require some form of transcription factor binding assay, e.g. ChIP-seq or CUT&RUN. I am fully aware that these assays are enormously challenging to perform in this system (and again I don’t suggest that these experiments need to be done for this work); however, statements of direct regulation should be tempered. This is especially true for the role of SP8. This does appear to be a compelling target, but without some manipulation of the activity of SP8 (e.g. through knockdowns) and subsequent analysis of gene expression, it is too much to claim that this transcription factor is a regulatory link in the testosterone-driven responses. SP8 does appear to be a highly connected hub gene in correlation network analysis, but this alone does not indicate that it acts as a hub transcription factor in a gene regulatory network.

We appreciate the reviewer's comment and have revised the statement concerning the role of SP8. Indeed, we document the coexpression of ESR2 and SP8, and our bioinformatics analysis suggests that SP8 might play an important role in transcriptomics. We have rephrased the statement in line 29-32 as follows: "Parallel gene regulation directly by androgen and estrogen receptors, potentially amplified by coexpressed transcription factors that are themselves steroid receptor regulated, leads to substantial transcriptomic and neural changes in specific behavior-controlling brain areas, resulting in the gradual seasonal occurrence of singing behavior." In addition, we have included discussions regarding limitations of promoter sequence analyses (lines 414 to 427).

1.3. Along these lines, the in-situ hybridizations of ESR2 and SP8 presented in Figure 5 need significant improvement. The signals in the red and green channels, SP8 and ESR2, look suspiciously similar, showing almost identical subcellular colocalization. This signal pattern usually suggests bleed-through during image acquisition, as it’s highly unlikely that the mRNA of both genes would show this degree of overlap. I would suggest that control ISHs be run with one probe left out, either SP8 or ESR2, and compare these ISHs with the dual label ISHs to determine if signal intensity and cellular distribution look similar. Furthermore, on lines 354-356 the authors write, "The fact that the two genes were expressed nearby in the same cell may indicate physical interactions between the gene pair and warrant further investigation into the nature of their relationship.". Yet, even if the overlap between ESR2 and SP8 shown in Figure 5 is confirmed, close localization of transcripts does not imply that the protein products physically interact. The STRING bioinformatic analysis is more convincing that there is a putative regulatory interaction between ESR2 and the SP8 locus, and this suggestion of protein-protein interaction is weak and should be omitted. In addition, the authors note that ESR2 has not been detected in the songbird HVC in a previous study. To further demonstrate the expression of ESR2 (and SP8) in HVC, it would be useful to plot their expression from the microarray data across the different testosterone conditions.

We repeated the coexpression study using confocal microscopy and fluorescent RNAScope in situ hybridization, which is now reflected in the revised Figure 5 and a new Figure 5 - Supplement Figure 1. We have also moderated our statement regarding the sparse co-expression of ESR2 and SP8 in HVC neurons. While the presence of co-expressing neurons may provide some anatomical basis for the bioinformatic findings, we have been cautious in our interpretation and have stated that "SP8 and ESR2 mRNAs exhibited low expression levels in HVC, co-localizing in a subset of cells, predominantly GABAergic cells" (lines 369-370). We have removed the speculation about potential protein interaction based on mRNA distribution. Additionally, we have highlighted that SP8 and ESR2 were differentially upregulated at T14d (lines 362-363).

1.4) My final concern lies in the interpretation of these results as generalizable to other sex hormone-modualated behaviors. On lines 452-455, the authors write, "This suggests that the testosterone (or estrogen)-triggered induction of adult behaviors, such as parental behavior and courtship, requires a much more extensive reorganization of the transcriptome and the associated biological functions of the brain areas involved than previously thought.". The experiments and argument likely apply to other neural systems to undergo large seasonal fluctuations in sex hormones and similar morphological changes. However, the authors argue that the large number of transcriptional changes seen here may generalize broadly to sex hormone modulated adult behaviors. I think there are a couple of problems with this argument. First, as described here and in past work, testosterone drives major morphological changes the song system of adult canaries; such dramatic changes are not seen for instance in sex hormone-receptive areas underlying mating behavior in adult mammals. Similarly, the study introduced testosterone into female birds which drives a greater morphological change in HVC relative to similar manipulations in males, which again may account for the large number of differentially expressed genes. I would temper the generality of these results and note how the experimental and biological differences between this system and other sex hormone-responsive systems and behaviors may contribute to the observed transcriptional differences.

We modified this statement in lines 473-478: “The testosterone-driven changes in female HVC morphology and function represent some of the most notable modifications known in the vertebrate brain. However, how this extensive, testosterone-induced gene regulation in the HVC applies to other seasonally testosterone-sensitive brain areas remains to be seen. Endpoint analysis of testosterone-induced singing in male canaries during the non-reproductive season also indicates considerable regulation of HVC transcriptomes (Frankl-Vilches et al., 2015; Ko et al., 2021)”.

Reviewer #2 (Public Review):

First, we would like to express our gratitude to Reviewer #2 for the constructive feedback. We have addressed the concerns in detail below:

2.1). The bulk of the manuscript details WGCNA, GO terms, and promoter ARE/ERE motif abundance, using the initial pairwise comparisons for each timepoint as input lists. However, there are no p/adjp values provided for these pair-wise comparisons that form the basis of all subsequent analyses. Nor are there supplementary tables to indicate how consistent the replicates are within each group or how abundantly the genes-of-interest are expressed. With the statistical tests used here, and the lack of relevant information in the supplementary tables, I cannot determine if the data support the authors’ conclusions. These omissions mar what is otherwise a conceptually intriguing line of investigation.

We appreciate the reviewer’s concerns. Please refer to our response addressing this point and the subsequent one (2.2) together in the section below.

Reviewer #3 (Public Review):

We appreciate the positive feedback from the reviewer and below addressed the issues pointed out by the reviewer.

3.1) My biggest concern is the sample size. Most of the time points only have 5 or 6 individuals represented, and I question whether these numbers provide sufficient statistical power to uncover the effects the authors are trying to explore. This is a particular problem when it comes to evaluating the supposed "transient" of testosterone on gene expression. There is currently little basis for distinguishing such effects from noise that accrues because of low power. This can be a major problem with studies of gene expression in non-model species, like canaries, where among-individual variability in transcript abundance is quite high. Thus, it is possible that one or two outliers at a given time point cause the effect testosterone at this time point to become indistinguishable from the controls; if so, then a gene may get put into the transient category, when in fact its regulation was not likely transient.

We acknowledge that our sample sizes may appear moderate. To address the concern regarding temporal regulation analysis, we followed Reviewer 3's suggestion and conducted a probe-level power analysis (point 2 of recommendations for the authors; labelled as point 3.9 below). We then excluded differentially expressed genes with a power less than 0.8 prior to conducting temporal classification. Consequently, 93% of our differentially expressed genes demonstrated a power ≥ 0.8 (9025/9710). Following further classification by temporal regulation pattern, we identified 29 constantly upregulated, 41 constantly downregulated, 39 dynamically regulated, and 8916 transiently regulated genes. If we apply a stricter constraint by requiring each differentially expressed gene to have at least two probe-sets with a power ≥ 0.8, 83% of differentially expressed genes (8033/9710) still have sufficient power.

We recognize that our sample size may not be sufficient to detect weakly differentially expressed genes. However, we have intentionally excluded these genes from the beginning (those with |log2(fold change)| ≤ 0.5 were excluded).

The scenario outlined by the reviewer, where outliers might cause the effect of testosterone to blend with controls, leading to misclassification, is indeed plausible. This could occur either because the genes are weakly regulated, or because the power to detect differential expression is insufficient, thus preventing these genes from surpassing the threshold to be deemed significantly differentially expressed. However, this also illustrates that the effect of testosterone does not regulate every gene in the same way.

We have appended a column indicating high power genes (≥ 0.8) in the DiffExpression.tsv file, available in the Dryad repository. The power analysis has been incorporated to the method section at lines 801-808 and result section at lines 188-192.

3.2) More on the transient categorization. Would a gene whose expression is not immediately upregulated (within 1 hour), but is upregulated later on (say in the 14d group) be considered transient? If so, this seems problematic. Aren’t the authors setting the null expectation of "non-transient" as a gene that does not increase immediately after 1 hour of treatment? The authors even recognize that it is quite surprising that gene expression changes after an hour. It may be that some genes whose regulation is classified as transient are simply slower to upregulate; but, really, would we say their expression in transient per se? Maybe I’m misunderstanding the categorizations?

We appreciate the reviewer's insightful discussion regarding the transient categorization. We understand that it is indeed more challenging for a gene to be classified as constantly regulated than transiently regulated, due to smaller effects by testosterone or being undetectable owing to low power. To address this concern, we further dissected the transiently regulated category by reporting the number of time points at which a gene is differentially expressed in Figure 2 - Figure supplement 1. Approximately half of the transiently regulated genes were only regulated at one time point, further illustrating that the effect of testosterone on gene expression was not constant during the time window we examined (see lines 184 - 187).

3.3) The authors don’t fully explain the logic for using females in this study to measure a "male-typical" behavior (singing). My understanding is that females have underlying circuitry to sign, and T administration triggers it; thus, this situation that creates a natural experiment in which we can explore T’s on brain and behavior, unlike in males which have fluctuating T. First, it might be good to clarify this logic for readers, unless perhaps I’m misunderstanding something. Second, I found myself questioning this logic a little. Our understanding of basic sex differences and the role that steroid hormones play in generating them has changed over the last few decades. There are, for example, a variety of genetic factors that underlie the development of sex differences in the brain (I’m especially thinking about the incredible work from Art Arnold and many others that harness the experimental power of the four core genotype mice). Might some of these factors influence female development, such that T’s effects on the female brain and subsequent ability to increase HVC size and sing is not the same as males.

Indeed, sex-chromosome dosage compensation is absent in birds leading to higher Z-chromosomal gene expression in males. We demonstrated substantial sex differences in gene expression in our earlier work [Ko, M.-C., Frankl-Vilches, C., Bakker, A., Gahr, M., 2021. The Gene Expression Profile of the Song Control Nucleus HVC Shows Sex Specificity, Hormone Responsiveness, and Species Specificity Among Songbirds. Frontiers in Neuroscience 15].

We have revised the introduction (lines 96-98) to clarify our rationale for using female canaries as a model for adult behavioral development, not as a model for male canaries. After testosterone treatment, these females start to sing, with song structure developing over time, similar to male seasonal progression. This approach eliminates the confounding effect of fluctuating testosterone levels seen in males, supported by distinct HVC transcriptomes in testosterone-implanted singing female canaries compared to males (Ko et al., 2021).

The revised paragraph reads as below: Female canaries (Serinus canaria) are typically non-singers, with their spontaneous songs displaying less complexity than their male counterparts (Hartley et al., 1997; Herrick and Harris, 1957; Ko et al., 2020; Pesch and Güttinger, 1985). Despite their infrequent singing, these females possess the necessary underlying circuitry that can be activated by testosterone. Following testosterone treatment, these females start to produce simple songs, which gradually evolve in structure over weeks—paralleling the seasonal progression of male singing (Hartog et al., 2009; Ko et al., 2020; Shoemaker, 1939; Vallet et al., 1996; Vellema et al., 2019). Moreover, testosterone induces the differentiation of song control-related brain nuclei in adult female canaries, a critical step for song development (Fusani et al., 2003; Madison et al., 2015; Nottebohm, 1980). In this study, we focus on these testosterone-treated female canaries as a model for adult behavioral development rather than a model for male canaries. This unique model allows us to examine transcriptional cascades in parallel with the differentiation of the song control system and the progression of song development, without the confounding impact of fluctuating testosterone levels seen in males, which often results in considerable individual differences in the non-reproductive season baseline singing behavior. This approach is backed by the observation that the HVC transcriptomes of testosterone-implanted singing female canaries are distinct from those of singing males (Ko et al., 2021).

3.4) I was surprised by the authors assertion that testosterone would only influence several tens or hundreds of genes. My read of the literature says that this is low, and I would have expected 100s, if not 1,000s, of genes to be influenced. I think that the total number of genes influenced by T is therefore quite consistent with the literature.

We apologize for any confusion caused by our statement. We did not mean to imply that testosterone only influences several tens or hundreds of genes, but rather that we did not expect such an extensive transcriptional regulation in the HVC by testosterone. We have clarified this in our revised manuscript, specifically in lines 450-451. Thank you for helping us to clarify this point.

3.5) I found the GO analyses presented herein uncompelling. As the authors likely know, not all GO terms are created equally. Some GO terms are enriched by hundreds of genes and thus reflect broad functional categories, whereas other GO terms are much more specific and thus are enriched by only a few genes. The authors report broad GO terms that don’t tell us much about what is happening in the HVC functionally. This is particularly the case when a good 50% of the genome is being differentially regulated.

We appreciate the reviewer's comment. We have added KEGG pathway enrichment analysis in Figure 3 - Figure supplement 1 as an alternative. However, we believe that the GO term enrichment results still provide valuable insights, and therefore we have retained them in Fig. 3.

3.6) The Genomatix analyses are similarly uncompelling. This approach to finding putative response elements can uncover many false positives, and these should always be validated thoroughly. Don’t get me wrong-I appreciate that these validations are not trivial, and I value the authors response element analysis.

We appreciate the reviewer's comment on the presence of AR or ER motifs in promoters and acknowledge that in mammals, AR and ER predominantly bind at distal enhancers rather than promoters. Our analysis focused on promoter regions due to the limitations of available tools and resources for our study species. We understand that this approach may not capture the full complexity of AR and ER regulation. We have revised our manuscript to note the limitations of our approach and clarify that the presence of AREs and EREs alone is not indicative of active receptor binding or direct regulation (lines 416-427).

3.7) I’m sceptical about the section of the paper that speculates about modification of steroid sensitivity in the HVC. These conclusions are based on analyses of mRNA expression of AKR1D1, SRD5A2, and the like. However, this does not reflect a different in the capacity to metabolize steroids, or at least there is little evidence to suggest this. Note that many of these transcripts have different isoforms, which could also influence steroidal metabolism.

We agree that mRNA expression levels of AKR1D1, SRD5A2, and other transcripts involved in steroid metabolism do not necessarily reflect changes in steroid metabolizing capacity. However, we believe that these changes in mRNA expression are indicative of potential changes in steroid sensitivity in the HVC, which could affect the neural response to steroids. We acknowledge that isoform differences of these transcripts may influence steroid metabolism and further studies are necessary to confirm our findings and elucidate the mechanisms underlying the observed changes in gene expression. In response to this comment, we have amended the text in lines 245-249 to reflect this consideration.

Reviewer #3 (Public Review):

I found this paper fascinating. It is a study that needed to be done in the field of behavioral endocrinology, as it addresses our understanding of exactly how steroid hormone action might regulate behavioral output like few other published studies. For decades, researchers have been implanting animals with steroids and observing corresponding changes in behavior, noting that some behavioral traits are immediately expressed, while others take time to be expressed. Why would this be? The answer lies in the temporal dynamics of steroid action, but few have ever addressed this. Having said this, I do have several issues with the manuscript that I think need to be addressed.

1) My biggest concern is the sample size. Most of the time points only have 5 or 6 individuals represented, and I question whether these numbers provide sufficient statistical power to uncover the effects the authors are trying to explore. This is a particular problem when it comes to evaluating the supposed "transient" of testosterone on gene expression. There is currently little basis for distinguishing such effects from noise that accrues because of low power. This can be a major problem with studies of gene expression in non-model species, like canaries, where among-individual variability in transcript abundance is quite high. Thus, it is possible that one or two outliers at a given time point cause the effect testosterone at this time point to become indistinguishable from the controls; if so, then a gene may get put into the transient category, when in fact its regulation was not likely transient.

2) More on the transient categorization. Would a gene whose expression is not immediately upregulated (within 1 hour), but is upregulated later on (say in the 14d group) be considered transient? If so, this seems problematic. Aren't the authors setting the null expectation of "non-transient" as a gene that does not increase immediately after 1 hour of treatment? The authors even recognize that it is quite surprising that gene expression changes after an hour. It may be that some genes whose regulation is classified as transient are simply slower to upregulate; but, really, would we say their expression in transient per se? Maybe I'm misunderstanding the categorizations?

3) The authors don't fully explain the logic for using females in this study to measure a "male-typical" behavior (singing). My understanding is that females have underlying circuitry to sign, and T administration triggers it; thus, this situation that creates a natural experiment in which we can explore T's on brain and behavior, unlike in males which have fluctuating T. First, it might be good to clarify this logic for readers, unless perhaps I'm misunderstanding something. Second, I found myself questioning this logic a little. Our understanding of basic sex differences and the role that steroid hormones play in generating them has changed over the last few decades. There are, for example, a variety of genetic factors that underlie the development of sex differences in the brain (I'm especially thinking about the incredible work from Art Arnold and many others that harness the experimental power of the four core genotype mice). Might some of these factors influence female development, such that T's effects on the female brain and subsequent ability to increase HVC size and sing is not the same as males.

4) I was surprised by the authors assertion that testosterone would only influence several tens or hundreds of genes. My read of the literature says that this is low, and I would have expected 100s, if not 1,000s, of genes to be influenced. I think that the total number of genes influenced by T is therefore quite consistent with the literature.

5) I found the GO analyses presented herein uncompelling. As the authors likely know, not all GO terms are created equally. Some GO terms are enriched by hundreds of genes and thus reflect broad functional categories, whereas other GO terms are much more specific and thus are enriched by only a few genes. The authors report broad GO terms that don't tell us much about what is happening in the HVC functionally. This is particularly the case when a good 50% of the genome is being differentially regulated.

6) The Genomatix analyses are similarly uncompelling. This approach to finding putative response elements can uncover many false positives, and these should always be validated thoroughly. Don't get me wrong-I appreciate that these validations are not trivial, and I value the authors response element analysis.

7) I'm sceptical about the section of the paper that speculates about modification of steroid sensitivity in the HVC. These conclusions are based on analyses of mRNA expression of AKR1D1, SRD5A2, and the like. However, this does not reflect a different in the capacity to metabolize steroids, or at least there is little evidence to suggest this. Note that many of these transcripts have different isoforms, which could also influence steroidal metabolism.

Author Response

Reviewer #1 (Public Review):

This manuscript confirms previous studies suggesting a great deal of heterogeneity of gene expression at the neural plate border in early vertebrate embryos, as neural, placodal, neural crest, and epidermal lineages gradually segregate. Using scRNA-seq, the study expands previous studies by using far larger numbers of genes as evidence of this heterogeneity. The evidence for this heterogeneity and the change in heterogeneity over time is compelling.

Many studies have suggested that there is considerable heterogeneity of gene expression in the developing neural plate border as the neural, neural crest, placodal and epidermal lineages segregate. Although the evidence for such heterogeneity was strong, until the advent of scRNA-seq, the extent of this heterogeneity was not appreciated. By using scRNA-seq at different stages of chick development, the authors sought to characterize how this heterogeneity develops and resolves over time.

The work is technically sound, and the level of analysis of gene expression, clustering, synexpression groups, and dynamic changes in gene modules over time is state-of-the-art. A weakness of the results as they stand now is that the conclusions of the analysis are not tested by the authors and thus, are over-interpreted. Such tests could be performed in future studies either by gain- and loss-of-function experiments or by using lineage tracing to demonstrate that the cell states the authors observe - especially the "unstable progenitors" they characterize - are biologically meaningful. The data will nevertheless be a useful resource to investigators interested in understanding the development of different cell lineages at the neural plate border.

We thank the reviewer for the positive assessment of our work. We agree that our models will need to be tested experimentally in the future, however, this will require a substantial amount of work. We therefore opted to share our data as a resource to be used by the community.

Reviewer #2 (Public Review):

The study of Thiery et al. aims to elucidate how cells undergo fate decisions between neural crest and (pan-) placodal cells at the neural plate border (NPB). While several previous single-cell RNA-Seq studies in vertebrates have included neural plate border cells (e.g. Briggs et al., 2018; Wagner et al., 2018; Williams et al., 2022), these previous studies did not provide conclusive insights on cell fate decisions between neural crest and placodes, due to either the limited number of genes recovered, the limited number of cells sampled or the limited numbers of stages included. The present study overcomes these limitations by analyzing almost 18,000 cells at six stages of development ranging from gastrulation until after neural tube closure (8 somite-stage), with an average depth of almost 4000 genes/cell. Using this extensive and high-quality data set, the study first describes the timing of segregation of neural crest and placodal lineages at the NPB suggesting that at late neural fold stages (somite stage 4) most cells have decided between placodal and neural crest fates. It then identifies gene modules specific for neural crest and placodal lineages and characterizes their temporal and spatial expression. Focusing on an NPB-specific subset of cells, the study then shows that initially most of these cells co-express neural crest and placodal gene modules suggesting that these are undecided cells, which they term "border-located unstable progenitors" (BLUPs). The proportion of BLUPs decreases over time, while cells classified as placodal or neural crest cells increases, with few BLUPs remaining at late neural fold stages (and a few scattered BLUPs even at somite stage 8). Based on these findings, the authors propose a new model of cell fate decisions at the NPB (termed the "gradient border model"), according to which the NPB is not defined by a specific transcriptional state but is rather a region of undecided cells, which diminishes in size between gastrulation and neural fold stages due to more and more cells committing to a placodal or neural crest fate based on their mediolateral position (with medial cells becoming specified as neural crest and lateral cells as placodal cells).

The study of Thiery et al. provides an unprecedentedly detailed, methodologically careful, and well-argued analysis of cell fate decisions at the NPB. It provides novel insights into this process by clearly demonstrating that the NPB is an area of indecision, in which cells initially co-express gene modules for ectodermal fates (neural crest and placodes), which subsequently become segregated into mutually exclusive cell populations. The paper is very well written and largely succeeds in presenting the very complex strategy of data analysis in a clear way. By addressing the earliest cell fate decisions in the ectoderm and one of the earliest cell fate decisions in the developing vertebrate embryo, this study will have a significant impact and be of interest to a wide audience of developmental biologists. There are, two conceptual issues raised in the paper that require further discussion.

We thank the reviewer for the positive comments on our work and its significance; we have addressed the conceptual issues below and in the revised version of the manuscript.

First, the authors suggest that their data resolve a conflict between two previously proposed models, the "binary competence model" and the "neural plate border model". The authors correctly describe, that the binary competence model proposed by Ahrens and Schlosser (2005) and Schlosser (2006) suggests that the ectoderm is first divided into two territories (neural and non-neural), which differ in competence, with the neural territory subsequently giving rise to the neural plate and neural crest and the non-neural territory giving rise to placodes and epidermis (sequence of cell-fate decisions: ([neural or neural crest]-[epidermal or placodal]). This model was proposed as an alternative to a "neural plate border state model", which instead suggests that initially the NPB is induced as a territory characterized by a specific transcriptional state, from which then neural crest and placodes are induced by different signals (sequence of cell fate decisions: neural-[placodal or neural crest]-epidermal) (see Schlosser, 2006, 2014). Instead in this paper, the authors contrast the binary competence model with a model they call the "neural plate border" model according to which the NPB can give rise to all four ectodermal fates with equal probability. However, I think this misses the main point of contention since all previously proposed models are in agreement that initially the neural plate border region is unspecified and can give rise to all four fates and that lineage restrictions only appear over time. "Binary competence" and "Neural plate border state" model, differ, however, in their predictions about the sequence, in which these fate restrictions occur.

We appreciate the reviewer's thoughtful feedback, but respectfully disagree with their comment regarding the sequence of events predicted by the neural plate border (NPB) model. While the NPB model does suggest that the NPB is a transcriptionally distinct state, it does not make specific predictions about the sequence of fate decisions. Although several papers cited in the Schlosser 2006 and 2014 reviews suggest that the NPB gives rise to all four ectodermal fates, none of them (and, to the best of our knowledge, no other primary paper referring to the NPB model) specifically defines the sequence of fate specification from the NPB.

The key points of the NPB model are that the NPB is defined by overlapping expression of early neural/non-neural markers (which is also observed in Xenopus – see Pieper et al., 2012 supplementary material), contains progenitors for all four ectodermal fates, and that this "state" exists prior to the emergence of definitive neural crest and placodal cells.

To investigate the heterogeneity in the order of cell fate decisions at the NPB, we carried out additional pairwise co-expression analyses of forebrain, mid-hindbrain, neural crest, and placodal gene modules, which reveals multiple different hierarchies of cell fate choice depending on a cell's axial positioning, as shown in Figure 6-figure supplement 1.

Considering these findings, we have expanded our discussion of the previously proposed binary competence and neural plate border models to highlight how neither of these models is sufficient to fully characterize the heterogeneity in cell fate decisions observed in our study. We hope this clarification will help address any concerns the reviewer may have had about the NPB model and its implications for our results.

Second, the authors should be more careful when relating their data to the specification or commitment of cells. Questions of specification and commitment can only be tested by experimental manipulation and cannot be inferred from a transcriptome analysis of normal development. So the conclusion that the activation of placodal, neural and neural crest-specific modules in that sequence suggests a sequence of specification in the same temporal order (lines 706-709) is not justified. Studies from the authors' own lab previously showed that epiblast cells from pre-gastrula stages are specified to express a large number of NPB border markers including neural crest and panplacodal markers, when cultured in vitro (Trevers et al., 2018; see also Basch et al., 2006 for early specification of the neural crest), which is not easily reconciled with this interpretation. I am not aware of any experimental evidence that shows that a panplacodal regulatory state is specified prior to neural crest in the chick (although I may have missed this). In Xenopus, experimental studies have shown instead that neural crest is specified and committed during late gastrulation, while the panplacodal states are specified much later, at neural fold stages (Mancilla and Mayor, 2006; Ahrens and Schlosser, 2005). It may well be the case that the relative timing of neural crest and panplacodal specification is different between species (and such easy dissociability may even be expected from the perspective of the binary competence model).

We very much agree with the reviewer that the definitions and correct terminology is important and apologise for lack of clarity. We have reworded the text carefully.

The reviewer is correct: specification of neural crest, placodes and neural plate is observed very early in chick, prior to gastrulation. However, in specification experiments tissue is removed from its normal environment to reveal what it does autonomously in the absence of additional signals. In the current study, we assess the activation of gene modules in normal development. We have therefore reworded the text to avoid ‘specification’ in this context.

Reviewer #3 (Public Review):

The goal of this work was to better understand how cell fate decisions at the neural plate border (NPB) occur. There are two prevailing models in the field for how neural, neural crest and placode fates emerge: (i) binary competence which suggests initial segregation of ectoderm into neural/neural crest versus placode/epidermis; (ii) neural plate border, where cells have mixed identity and retain the ability to generate all the ectodermal derivatives until after neurulation begins.

The authors use single-cell sequencing to define the development of the NPB at a transcriptional level and suggest that their cell classification identified increased ectodermal cell diversity over time and that as cells age their fate probabilities become transcriptionally similar to their terminal state. The observation of a placode module emerging before the neural and neural crest modules is somewhat consistent with the binary competence model but the observation of cells with potentially mixed identity at earlier stages is consistent with the neural plate border model.

Differences in the timing of analyses and techniques used can account for the generation of these two original models, and in essence, the authors have found some evidence for both models, possibly due to the period over which they performed their studies. However, the authors propose recognizing the neural plate border as an anatomical structure, containing transcriptionally unstable progenitors and that a gradient border model defines cell fate choice in concert with spatiotemporal positioning.

The idea that the neural plate border is an anatomical structure is not new to most embryologists as this has been well-recognized in lineage tracing and transplantation assays in many different species over many decades.

We appreciate the reviewers comment and agree that the neural plate border has previously been characterised anatomically. However, many studies have applied the term literally in reference to a transcriptional state which is specified through the expression of ‘neural plate border specifiers’, prior to segregation of the placodes and neural crest. Here we highlight that treating the neural plate border as a definitive transcriptional state which can be identified through the expression of ‘neural plate border specifiers’ is false. Instead, we find these ‘specifiers’ are upregulated within either neural crest, placodal or neural cell lineages over time. Cells at the neural plate border co-express these alternate lineage markers and therefore predicted to be undecided.

The authors don't provide molecular evidence for transcriptional instability in any cells. It's a molecular term and phenomenon inaccurately applied to these cells that are simply bipotential progenitors.

We thank the reviewer for pointing this out; we have therefore refrained from using the term unstable and instead refer to the cells as ‘undecided’ as suggested by reviewer 2.

Lastly, there's no evidence of a gradient that fits the proper biochemical or molecular definition. Graded or sequential are more appropriate terms that reflect the lineage determination or segregation events the authors characterize, but there's no data provided to support a true role for a gradient such as that achieved by a concentration or time-dependent morphogen.

We agree with the reviewer that ‘gradient’ was misleading. We have now replaced ‘gradient’ with ‘graded’ and expanded figure 6 to highlight the graded co-expression of gene modules associated with alternate fates. We have changed the title to reflect this.

A limitation of the study is that much of it reads like a proof-of-principle because validation comes primarily from known genes, their expression patterns in vivo, and their subsequent in vivo functions. Thus, the authors need to qualify their interpretations and conclusions and provide caveats throughout the manuscript to reflect the fact that no functional testing was performed on any novel genes in the emerging modules classified as placode versus neural or neural crest.

We agree with the reviewer that we do not provide any functional data to validate our predictions; it is for this reason that we submitted the manuscript as a ‘resource’ to make our data available to the community.

Lastly, a limitation of gene expression studies is that it provides snapshots of cells in time, and while implying they have broad potential or are lineage fated, do not actually test and confirm their ultimate fate. Therefore, in parallel with their studies, the authors really need to consider, the wealth of lineage tracing data, especially single-cell lineage tracing, which has been performed using the embryos of the same stage as that sequenced in this study, and which has revealed critical data about the potential cells through when and where lineage segregation and cell fate determination occurs.

The reviewer rightly points out the significance of the classical experiments in the context of the neural plate border. However, only one of the mentioned studies (Bronner-Fraser and Fraser, 1989), analyses cells at a single-cell level and does not assess placodes, while the remaining studies use tissue transplantation or cell population labelling. Although these studies provide valuable insights, they do not examine the fate or potential of single cells, nor do they reveal the transcriptional signature of these progenitors.

Our findings emphasize the transcriptional heterogeneity at the neural plate border, suggesting that distinct subsets of neural plate border progenitors undergo varying sequences of fate restrictions. The upcoming challenge will be to conduct clonal analysis alongside scRNAseq to determine if neural plate border progenitors with similar transcriptional signatures experience the same fate restrictions or if external factors, such as cell-cell signalling, dictate cell fate choices.

We have amended the manuscript to clarify that predictions of fate decisions require future validation through lineage tracing. Additionally, we have acknowledged in the introduction that previous studies have demonstrated the intermingling of neural, neural crest, and placodal progenitors at the neural plate border.

Author Response

Reviewer #2 (Public Review):

Kim et al. examined the properties of neuronal connections responsible for inhibitory cell activation to show that the characteristics examined were similar in humans and rodents. This is important, as it suggests that the many rodent studies carried out over the past decades are physiologically relevant to humans.

Strengths

1) Human brain tissues are difficult to obtain, hence the study provides valuable insights

2) An impressive multipronged approach was used for cell classifications

3) Despite the lack of novel findings, the revelation of the similarities between human and rodent synapses is important and has far-reaching implications. This important finding suggests the knowledge generated from rodent research is, at least partly, physiologically relevant to and transferrable to humans.

Weaknesses

1) The study is descriptive by design, and hence provides limited conceptual advances, especially with the retrospect that synaptic properties are similar between humans and rodents (although see strength #3). For example, very similar findings and techniques have already recently been reported by a number of the same authors in the Campagnola et al., Science 2022 paper.

We agreed that stimulus protocols of connectivity assays with multiple patch-clamp recordings in this study had been adapted from the recent publication (Campagnola et al., Science 2022). In this previous study, especially for human synaptic connectivity data, the main cell type categorization was at the level of excitatory and inhibitory neurons which identified based on morphological features and observed PSP characteristics (e.g., direction of membrane potential changes) when it connected each other. However, we went further to identify interneuron subclasses in the connectivity assays using virally labeled slice cultures and post-hoc HCR staining in addition to intrinsic classifier, which is not investigated from the recent publication (Campagnola et al., 2022). Therefore, following scientific findings and their implications are not the same shown in the previous study and we think this study provides a significant advance of our understanding in human cortical circuits organization.

2) Despite the fact that normal physiology was reported, the use of pathological human brain tissue could affect the results.

We agreed that the use of pathological human brain tissue to investigate normal physiology is not ideal, however, as mentioned in the METHODS below (section of “Acute slice preparation”), our surgically resected neocortical tissues show minimal pathology, and we believe these tissue preparations can be used to address normal physiological properties of human neurons. Importantly, we saw no effect of disease state (epilepsy vs. tumor) on the intrinsic or synaptic properties that we measured. Our METHODS state that “Surgically resected neocortical tissue was distal to the pathological core (i.e., tumor tissue or mesial temporal structures). Detailed histological assessment and using a curated panel of cellular marker antibodies indicated a lack of overt pathology in surgically resected cortical slices (Berg et al., 2021).”. We also state in the RESULTS that “These tissues were distal to the epileptic focus or tumor, and have shown minimal pathology when examined (Berg et al., 2021). Brain pathology was evaluated using six histological markers that were independently scored by three pathologists. Surgically resected tissues have been used extensively to characterize human cortical physiology and anatomy (Berg et al., 2021).”. Lastly, this is the best possible human tissue available for us to conduct physiological experiments. It is an unavoidable caveat of this work that our healthy brain tissue was derived from a donor brain exhibiting a serious disease.

3) The manuscript may not be easy to understand for the uninvited, because many concepts and abbreviations were not properly introduced.

Thank you for pointing this oversight out. We updated our manuscript and made sure that we fully describe all abbreviations. We now changed the abbreviation of MPC back to multiple patch-clamp recording, and some other abbreviations such as LAMP5, SLC17A7, DLX are now better explained. We have also changed the order of multiple figures (i.e., Figure 5 – Figure supplements to Figure 3 – Figure supplements) and removed some complicated figures (e.g., Figure 1 – Figure supplement 1) to present the data in a fashion that can be understood by a more general reader.

4) The statistical treatment is not ideal, so some conclusions may not be valid.

We performed additional statistical analyses as suggested and implemented in the text of the RESULTS.

Furthermore, we also made additional Figure supplements (Figure 4 – Figure supplement 3, Figure 4 – Figure supplement 4, Figure 6 – Figure supplement 2, and Figure 6 – Figure supplement 3) to support our conclusions.

5) The mixed usage of acute and cultured slices is not ideal and likely affects the outcome.

We agree that the mixed usage of acute and cultured slices is not ideal, and it could affect the interpretation of outcome. Therefore, we performed additional analyses to see if there is any correlated change of synaptic property (i.e., paired pulse ratio) along the days after slice culture (now implemented in Figure 4 – Figure supplement 4 and Figure 6 – Figure supplement 3) and we didn’t find any significant correlation. However, we noticed the short-term synaptic dynamics are rather differentiated between acute and slice culture condition shown in Figure 4 – Figure supplement 1d. We think this is due to sampling bias rather than tissue preparation difference and these points are now more carefully described in the DISCUSSION as “This difference we observed in this study, i.e., more facilitating synapses were detected in slice cultures than in acute slices, could either reflect an acute vs. slice culture difference. However, we believe it is more likely to reflect a selection bias for PVALB neurons when patching in unlabeled acute slices, and that the AAV-based strategy with a pan-GABAergic enhancer allows a more unbiased sampling of interneuron subclasses whose properties are preserved in culture. In support of this, PPR analysis as a function of days after slice culture shows no relationship to acute versus slice culture preparation (Figure 4 – Figure supplement 4, Figure 6 – Figure supplement 3). Furthermore, we have observed that viral targeting of GABAergic interneurons greatly facilitates sampling of the SST subclass in the human cortex compared to unbiased patch-seq experiments (Lee et al., 2022), and this selection bias likely explains synapse type sampling differences in cultured slices compared to acute preparations.”.

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Referee #3

Evidence, reproducibility and clarity

Summary

In this manuscript, Wang and colleagues demonstrate that a single systemic injection of a high dose of Akkermansia muciniphila (A.m.) lysate drives a rapid pancytopenia followed by prolonged anaemia and hepatosplenomegaly with late-onset extramedullary hematopoiesis (EMH). The latter, as well as the splenomegaly, were likely mediated through activation of pattern recognition receptors and IL-1R signalling pathways. This was demonstrated through the partial and full phenotype reversal in Tlr2;4-/- and MyD88;Trif-/- mice, respectively. Moreover, the phenotype was partially reversed following IL-1R antagonism. After performing multiplex protein assays and flow cytometry, the authors conclude that EMH, in this model, is mediated by IL-1a produced within the spleen by local monocytes and DC.

Overall, the manuscript by Wang et al. is quite well presented, the experiments are mostly well controlled, the methods are well reported, and the data fit a clearly defined story with clinical relevance. Nevertheless, there are several major concerns that if addressed would greatly increase the strength of the authors conclusions.

Major comments

1. The "two wave" hypothesis of hematopoiesis - first in the bone marrow (BM) and then in the spleen - is interesting. However, although an early wave of BM hematopoiesis would make sense, under these circumstances, I don't think the data are strong enough to support this hypothesis as they stand. For example, although the frequency of LSK cells increase, the numbers of most LSK subsets decrease. Given the decrease in the absolute number of BM cells 1d after A.m. injection, isn't it possible that the LSK cells are only proportionally increased relative to the remaining Lin- cells? What happens to the absolute number of LSK cells following A.m. injection?

Also, describing "two distinct waves of HSPC increase in the A.m.-injected spleen" (Fig 2 & S2 titles) and describing a "first wave" of HSPC expansion in the BM (lines 396, 399, 402 etc.) is misleading for the following reasons: (i) the data strongly support a single wave of increasing HSPC in the spleen, peaking at d14, and (ii) there is no evidence HSPC are increased in the BM until d56, although there does appear to be an early increase in MPP. The language should be changed accordingly. 2. The flow cytometry panel is not comprehensive enough to fully characterize the mature hematopoietic cell populations to the levels that are claimed here. For example, it is a stretch to assume that all B220- CD3- CD11c- cells are DC (splenic NK cells, eosinophils, monocytes and red pulp macrophages, for example, can express CD11c, particularly following inflammatory insult), or that CD11b+ F4/80+ SSC-hi cells are eosinophils, especially when eosinophils should be F4/80-lo are not known to express Ly6C in the spleen (For reference, see Immgen). These gating issues may explain the conspicuous absence of macrophages (should be F4/80+CD11b+Ly6C- and would also have a higher SSC than monocytes) in the plots. The B cell gate will also contain PDC, which express B220 (but can be easily excluded using Ly6C and CD11c). With respect to assessing the mature leukocyte populations in the spleen, relabelling the gates (CD11c+ cells instead of DC, F4/80+ myeloid cells instead of eosinophils) would suffice, however, these issues become a problem when trying to identify which cell populations express IL-1a.

Due to the limited antibody panel used here, there is not enough evidence to suggest that DC and monocytes are producing IL-1a. Moreover, the histograms showing the changes in expression of IL-1a on the "DC" and "Mo" are not very convincing. How does the IL-1a staining look on a dot plot? Is there good separation between positive and negative? These plots need to be included. What happens if you gate on the IL-1a+ cells first, then phenotype them?

Macrophages and splenic stromal cells are also likely candidates for IL-1a production. To assess which cell types are the true source of IL-1a, the authors need to repeat these experiments (namely, injecting A.m. and assessing IL-1a expression by leukocytes (and ideally also mesenchymal cells)) at d1 and d14, using a more comprehensive panel. Consider adding MHCII, CD64, Siglec F and CD24 to help differentiate between DC, MF, eosinophils and monocytes. CD45+ vs CD45- could be used as a minimum to assess the expression of IL-1a on leukocytes vs. stroma.

OPTIONAL: The mechanism could be better defined using bone marrow chimeras to assess the different contribution of TLR2/4 signalling and IL-1R signalling on the hematopoietic vs. mesenchymal cell compartments. 3. From these experiments, it is difficult to fully rule out a contribution from the adaptive immune system to the splenomegaly phenotype due to the marked difference in the size of BALB/c and MSTRG spleens at steady state. The authors should show the differences in spleen weight and total cell number as a % increase from control. The no of HSPC should also be normalized per gram of tissue weight or represented as a fold change compared to the relevant control groups. 4. When using fluorescent imaging to compare the abundance of HSPC and other cell populations in the spleen, the authors should provide absolute quantification from multiple FOV and multiple mice. 5. Finally, although the experiments are adequately replicated, the stats are not always appropriate. For example, a t-test shouldn't be used when there are >2 groups, or for a time course. This needs to be amended.

Minor comments

• Line 82-83: I'm fairly certain monocytes and inflammatory Ly6Chi cells are the same thing.
• Line 83-84: "IL-1a is crucial for sustaining inflammatory responses, recruiting myeloid cells to infected tissue and inducing hematopoietic stem and progenitor cell (HSPC) mobilization and expansion both in vitro and in vivo" - I don't believe IL-1a has been shown to be crucial for either, even if it has been shown to play a role. If I am mistaken, please reference with a manuscript showing relevant phenotypes using KO mice.
• Line 214: "Thus, we decided to use 200ug of lysate for the rest of all experiments." - is this what was usen for Figures 1A-C? This is not mentioned anywhere.
• Line 227: "containing both non-hematopoietic cells and immature HSPCs" Please reference Fig. 1H here. Otherwise, it is unclear how you identified the "HSPC and other cell types" in Fig. 1G.
• Figure S2A is described in text before Supp 1I-O and Fig S1H is not referenced in text at all.
• It would be interesting to include what happens to hepatomegaly in MSTRG, Tlr2;4-/- and MyD88;Trif-/- mice.
• Please define WBM. Presumably whole bone marrow?
• Notably, CCL2 is increased in spleen lysate, BM lysate and serum. Given is role in myeloid cell mobilization from the BM, I would expect its role in the phenotype described here to at least be discussed.
• HSPC LT gate includes MPP1, and should be labelled as such.

Significance

General assessment: The manuscript provided by Wang et al. describes, for the first time, a prolonged anaemia and hepatosplenomegaly with late-onset extramedullary hematopoiesis following a single systemic injection of A.m. lysate. The EMH phenotype appears robust and the data implicating TLR-signalling and IL-1a production are compelling. The work has clinical relevance as it increases our understanding of the factors driving EMH.

There are two key limitations that let this study down. Firstly, the lack of depth in the flow cytometry panel used for immunophenotyping means it is not at all clear which cell types are producing IL-1a. Secondly, the authors use an enormous dose of bacterial lysate that is well above physiological levels, even following a loss of barrier integrity (e.g., in patients with IBD). This makes me question the biological relevance of the study, particularly with respect to Akkermansia translocation.

Advance: With some improvement, this study will advance the field, in general. Previous work has looked at EMH following LPS injection, or live E. coli infection, however; the authors are able to demonstrate a distinct Akkermansia-specific effect that differs to that of LPS, membrane components of a different gram-negative bacteria, B. theta. The advancements implicate IL-1a in the modulation of EMH, for the first time, providing some mechanistic insight into this phenomenon.

Audience: This work will likely be of interest to basic researchers interested in EMH. It may also be of interest to clinical researchers of pathologies where EMH is a known complication, such as rheumatoid arthritis and cancer. The impact of the work will depend on whether or not EMH contributes to pathogenesis, or is an epiphenomenon. To my knowledge, this has not been fully established, although this is not my area of research.

I am a basic researcher with expertise in immunology focused on host-microbe interactions, both within the intestine and at distal tissues. I have knowledge of BM hematopoiesis and the microbial factors that influence if although my knowledge on extramedullary hematopoiesis is limited.

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Reply to the reviewers

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

The manuscript presents a detailed numerical model of blood flow in a region of the zebrafish vasculature.

The results section is quite intense and detailed. it is difficult to understand what the authors are after. I think a rewrite would beneficial. The authors present simulations for a wild type and a couple of phenotypes. For each of these they speculate on the possible adaptation mechanism leading to the discussed phenotype, as preservation of constant wall shear stress. However, the comparison between experiments and numerical simulations is really elusive as the conclusions on those mechanisms. Overall we suggest a rewrite with clearer organisation in a way that the reader is not overflown with useless details.

We thank the reviewer for the advice on the general writing standard and data organization. We have reanalyzed experiment data and interpreted the findings more conservatively for application into the simulation models. As a result, some conclusions to the results sections have changed. Accordingly, we have done a major revision of the entire Results, Discussion and Models and Methods sections in the paper to articulate these reinterpretations while removing superfluous details that may obfuscate the data.

It is not always clear what info of the experiments are used in the simulations on top of the anatomy. Our understanding is that the pressure boundary conditions are set to match the red blood cel velocity observed in experiments. Is this always the case for the three phenotypes and which vessels ?

We thank the reviewer for the question. Only WT and Marcksl1 KO have been matched for peak velocities in the CA, CV and ISVs between experiments and simulations. WT results were compared to both the experimental reference of 27 embryos in Table 3 and also to the current experiment pool of WT (5 embryos) in Table 6. Marcksl1 KO simulation models 1, 2 and 3 were compared against the average level seen in the low and moderate perfusion Marcksl1 KO phenotypes (8 embryos) from the experiment (Table 5 and Table 6). Additionally, we also have represented the similar level of RBC hematocrit in the CA for WT model to WT experiment data from the reference cited in Table 3.

In addition to the velocity comparisons, we now use the experimentally observed trend of decreased flow rate in the CA of Marcksl1 KO experiment data to assess the model boundary conditions amongst Marcksl1 KO models 1, 2 and 3 that best reflect the experimental observations:

Page 11, lines 1 to 20

The Marcksl1 OE cannot be matched because we do not have the experiment data for that, the same goes for PlxnD1 where we have no experiment flow data. These two networks represent more conceptual discussions, particularly in PlxnD1 case where we have explicitly stated in the new discussion section:

Page 15, lines 24 to 34

There are about 7 inlets and outlets where to impose pressure boundary conditions. Can the author comment on the uniqueness of this problem?

Can different combination of pressure boundary condition leading to the same result ? In how many points/vessels is the measured velocity matched ?

We thank the reviewer on this insightful concern. Indeed, the uniqueness of flow and pressure field can be a problem without careful consideration. We have tried to address this to some extent, because CA, CV are connected by the ISV and DLAV network, to match flow velocity in all regions, the pressure distribution ought to be unique to the particular setting we employed.

As shown in table 3, average systolic peak flow velocities in the entire CA and CV encompassing the 5 ISV segment domain is matched between the simulation and the population-averaged experimental data from the experimental reference (27 fish sampled in the cited reference) for the same regions in WT network. Average systolic peak flow velocities for the 10 ISVs in the simulation were matched against WT experiment population-averaged systolic peak flow velocities in arterial and venous ISVs in the same caudal region.

Additionally, we also compared the flow velocities to the experiment conducted within this study (5 WT, and embryos). This comparison data is shown in Table 6. Admittedly the discrepancy was large for CV and ISVs regions likely due to a smaller data set sampled in this study and biological variations that happen from one experiment to another. We have acknowledged this deficiency in the revised discussion section:

Page 15, lines 3 to 9

The argument that similar beating frequency in the WT and GATA1 MO suggest pressure does not change is not clear. If the heart was a volumetric pump it would impose the same flow rate, not the same pressure. It would be more useful to measure the cardiac output in terms of flow rate in the Dorsal Aorta. Previous measurements by Vermot suggested the latter would not change much in gata1 MO. It could be that the cardiac output is the same but the vasculature network is different in a way that the shear stress remain the same. It does not look like this was checked by the authors.

We thank the reviewer for this insight. In accordance with the reviewer’s suspicion, we have estimated the flow rates in the CA of gata1 MO injected embryos and found the level to be similar to WT. This supports the reviewer’s opinion that the heart rate similarity indicates cardiac output similarity and not arterial pressure similarity as we previously put forward. Furthermore, we have checked that the gata1 morphants do in fact present reduced ISV diameters. In light of this reinterpretation, we performed an additional zero hematocrit model (model 3 in section 2.1). We have consequently rewritten the entire section on how RBC hematocrit modulates hemodynamics in a microvascular network:

Page 6, line 18 to page 8 line 10.

Additionaly, it would be useful to provide an effective viscosity for the different vessels, and an effective hydraulic impedance relating DP and Q to interpret the results.

We have followed the reviewer’s advice and have analyzed for vessel hydraulic impedance and effective viscosity in all the network models presented. This is included in the main figures and discussion. The vessel impedances are discussed for the various models in these following parts of the manuscript:

Page 9, lines 20 to 29

Page 11, lines 28 to 30

Page 12, line 1 to page 13 line 10

Is the hydraulic impedance of the vessels kept constant in the smooth-geometry model? This needs clarification

The SGM diameters have been determined based on geometric averages and not impedance equivalency. The reason why we did this is because the impedance will not be known until the CFD is performed for the WT network. This is because without a pressure distribution (which cannot be determined experimentally) we cannot calculate vessel impedance since only flow can be measured and both flow and pressure are requirements to impedance calculation. Our intention with the SGM is to highlight how geometric averaging of morphological characteristics lead to incorrect flow and stress predictions. However, we understand the reviewer’s sensibility and have revised the entire section of the SGM results. We have now discussed three SGM models with varying degrees of geometry simplification. The SGM1 in the revised manuscript matches WT network impedance in the ISVs by including both axial variation in lumen diameter of the WT network and the elliptical fit representation of cross-sectional skewness seen in WT ISV lumens. SGM 2 has representation of axial variation but not luminal skewness and SGM3 has only geometric average similarity to WT ISVs. The new findings and discussion can be found in the revised manuscript here:

Page 8, line 19 to page 9 line 36.

As mentioned by the authors they propose a very complex and time expensive simulation. However the results they report are kind of intuitive. Given the availability of the experimental results, would it be useful to use a simpler red blood cell model in the future, to make their simulation more practical? Or clarify when such demanding simulations can add something new?

We agree that the intuition feedback depends on the expertise of the investigator. The boundary condition selection is intuitive from the experimental findings and key data like pressures in the network cannot be measured. Furthermore, population-averaged flow data does not always match the flow-to-geometry situations that vary from sample to sample, thus demonstrated by the high margin of prediction discrepancy for flow velocities in table 6. We have discussed these challenges and our recommendations for improvement in the Discussion section:

Page 15, lines 3 to 9

Page 15, lines 35 to 40

Page 16, lines 12 to 15

On the topic of RBC model simplification, we agree with the reviewer that our work suggests the methodology would benefit from a further coarse-graining approach to the RBC phase. Accordingly, we discussed the possibility of using a low-dimensional RBC model already published in literature:

Page 14, lines 13 to 17

The authors should check their references as this is not the first time work has been done on the topic. Would be good to have a check in the work of Freund JB and colleagues, as well as Dickinson and colleagues and Franco and colleagues to discuss how the work compares. There may be interesting work in modelling cardiac flow forces in the embryo too.

Thank you for referring us to other publications that are related to our study. To our knowledge and after performing publication search on these authors, we find that although Dickinson and colleagues performed experiments to examine the effects of perturbed blood flow on vessel remodelling (Udan et al., 2013), they did not perform any numerical modelling to calculate hemodynamic forces such as WSS and luminal pressure. Instead, changes in vessel morphogenetic process were only correlated with blood flow velocity. In our study, we attempt to quantitatively correlate WSS and pressure distributions within a vascular network. Franco and colleagues (Bernabeu et al., 2014) developed PoINet to model haemodynamic forces in mouse retina model of angiogenesis. From what we understand, PoINet is different from our 3D CFD model by 1) not having red blood cells incorporated in their model and as such, the blood viscosity prediction is modelled using shear-rate dependent formulation and not through red blood cell hematocrit, 2) cross sections of blood vessels are assumed to be circular and therefore have no irregularity and 3) live imaging of blood flow is difficult in mouse retina therefore preventing accurate boundary conditions for the model.

We have included the reference to work of Franco and colleagues:

Page 14, line 28 to line 31

Page 9, lines 12 to 14

Freund JB indeed has had extensive work on RBC and cellular flow in microvessels. We have included a reference of his work in:

Page 14, lines 22 to 25.

Reviewer #1 (Significance (Required)):

The authors discuss the applicability of a detailed numerical model of blood flow in a region of the zebrafish vasculature.

We are not expert in the lattice boltzmann method used here, but the results are what it would be expected from a physical stand point, and together with the information from the method section, we do not have major concerns about the numerics.

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

Summary: The authors report corroborating numerical-experimental studies on the relationship between morphological alterations (e.g. vessel lumen dilation/constriction, network mispatterning) and hemodynamical changes (e.g. variation in flow rate, pressure, wall shear stress) in the vascular network of zebrafish trunk circulation. Various physiological or pathological adaptation scenarios were proposed and tested, with a range of simulation and experiment models. Where I found it a solid piece of work supported by abundant data, certain aspects need to be clarified/enhanced to improve the scientific rigor and potential impact of the manuscript. Below are my detailed comments in the hope of helping the authors improve the manuscript's quality.

Major comments:

1. Cellular blood flow in vascular networks has been extensively studied in recent years by existing computational models (some of which were published open-source) with similar methods and features to the one proposed by the present work. Can the authors be more explicit about the original contributions of the current model, and provide evidence accordingly (e.g. Github repository or code resources)

The RBC model is essentially the model developed by Fedosov and colleagues (Fedosov, et al., 2010). Likewise, the LBM solver for fluid flow calculation is not. Following the reviewer’s advice, we have removed the details of these non-novel aspects of the methodology and placed them in sections E and F of supplementary material instead. The new Models and methods now show condensed descriptions of the three numerical solvers used and the addition of a grid independence matrix discussion section:

Page 17, line 8 to page 20, line 33.

Crucial details for the simulation setup and model configuration are missing. What were the exact boundary conditions (e.g. inlet and outlet pressures) and initial conditions (e.g. feeding hematocrit of RBCs), and how the numerical-experimental validation process of "to match the velocities of various segments of the network by iteratively altering the pressure inputs ..." as stated on page 13 (lines 1-2) was performed for simulations in this work?

We apologize for the vagueness of our description on how numerical to experimental validations were performed. As replied to reviewer 1 for a similar clarification, we have indicated in Table 3 how average systolic peak flow velocities in the entire CA and CV encompassing the 5 ISV segment domain were matched between the simulation and the population-averaged experimental data for the same regions in WT network. Average systolic peak flow velocities for the 10 ISVs in the simulation were matched against WT experiment population-averaged systolic peak flow velocities in arterial and venous ISVs in the same caudal region.

With regards to what iterative alterations of pressure inputs mean, we monitored the average systolic peak velocities and hematocrit levels in CA, CV and ISVs in intervals of 5 cardiac cycle intervals before manually correcting the pressure input levels to better match average systolic peak velocities in these vessels from the experiment averages. Since we are using population averaged flow data, we do not expect their levels to match the levels in a particular fish-specific geometry, the degree of discrepancy between experiment averages and the model predictions of systolic velocities can be large (Table 6). Admittedly, this is one of the weaknesses of our approach and this limitation is stated in the Discussion section:.

Page 15, lines 3 to 9

As RBC flow typically requires roughly 5 cardiac cycles of flow to reach flow development this process of iterative correction typically takes place over 10 to 20 cardiac cycles. We understand that validation may be a subject of keen interest to readers, hence we have now briefly described the solution initialization and flow development protocol in our modeling approach here:

Page 6, lines 5 to 8

What lattice resolution was used for the flow solver and was the RBC membrane mesh chosen accordingly? Were there any sensitivity analysis (regarding pressure input) or grid-independence study (regarding lattice resolution)

We originally decided on the grid (∆X) and time (∆T) discretization resolutions (0.5 µm and 0.5 µs) based on the acceptable computing turnaround time for each model within our scale of resources. We have now included a section on the grid independence matrix in Models and Methods:

Page 19, line 20 to page 20, line 33

Details of the statistical tests (type of tests used, assessment of data normality, sample size etc.) should be given in the figure caption where applicable (e.g. Fig. 3C, Figs. 7-9).

We apologize for the lack of clarity. All statistical tests used have now been mentioned at least once in each section of results and also in Figure captions wherever significance bars are displayed.

The regression models should also be used with caution, e.g. in Fig. 4B, why should data from two different fish types, namely Gata1 MO and WT, be grouped to fit a linear regression model?

We understand the reviewer’s concern that two population data sets should not be carelessly pooled together for regression analysis without adequate justification. In this case we are utilizing gata1 morpholino injection as a means to alter hematocrit level. There is no reported side-effect as to the best of our knowledge, only hematocrit and possibly hemodynamics and morphological response related to hematocrit level should be affected. Moreover, we have mislabelled the companion set to the gata1 morpholino as WT, the data is in fact data from control morphants and not WT. This change has been applied to Fig. 3 graphs and Table 4 and results section:

Page 7, lines 3 to 16

Finally, as we want to generate a continuum range of varying hematocrit for embryos of the same developmental age. In this regard, we think that within the scope of our intentions and well-accepted usage of gata1 morpholino as a hematocrit reduction protocol it is reasonable to pool the two data sets together for regression analysis.

4.I found the data presented in Fig. 7 insufficient to confidently exclude the numerical models 2, 3 but favor model 1 as the adaptation scenario for the Marcksl1KO case. The first question is, how are the threshold RBC perfusion levels determined to categorize the experimented Marcksl1KO fishes into four groups, i.e. "high", "moderate", "low", "zero"? The authors also need to justify why the "high", "moderate", "low" groups can be mapped to the three modelling scenarios (namely models 1, 2, 3) is it just because "a qualitative match with the experimental trend of ascending CA blood velocity" (Fig. 7F)?

We thank the reviewer for his interpretation of our results. Firstly, we apologize for generating the confusion but we are not trying to map simulation models 1, 2 and 3 to high moderate and low groups respectively in Fig. 7. The high, moderate and low categorizations of experimental Marcksl1 KO phenotypes are based on RBC flux levels observed experimentally. We are trying to ascertain which Marcksl KO phenotype the models 1, 2 and 3 fit, if they do fit the experiment trend at all.

Second, in Fig. 7C, it is shown that no significant difference exists between the "high" group and the WT in their average ISV diameter, then what is defining that group as Marcksl1KO type ?

We apologize for the confusion generated. High flow phenotype is similar to WT flow, the diameter is also similar to WT. In Marcksl1 KO mutants we don’t always see clear phenotyping and often a range is presented from mutant to mutant. Hence the high group is essentially morphometrically and hemodynamically similar to WT, the only reason we know it is a mutant because we have genotyped the zebrafish (marcksl1a-/-;marcksl1b1-/-).

Third, a central assumption here is using heart rate as a measure of the pressure drop in different fish individuals (Fig. 7D). Can't two fishes with similar heart rate have distinct pressure drops in the trunk due to difference in network architecture and topology, vice versa?

We agree with the reviewer’s opinion and now feel that our initial proposition was naïve. After addressing the interpretation of heart rate similarity in the gata1 morphants with more convincing CA flow rate estimations, we now believe that heart rates might not be useful indicators of flow or pressure levels in the network. Instead, cardiac output in the form of CA flow rate as reviewer 1 has suggested might be a better indicator. As the reanalysis has dismantled the earlier interpretation, and found that based on the flow rate estimation for the CA, Marcksl1 KO networks have reduced blood flow rates in the CA.

Page 11, lines 9 to 20

This finding has been incorporated into the consideration of flow adaptation scenarios predicted by the simulation models accordingly in the revised manuscript:

Page 12, line 1 to page 13, line 10

Fourth, the authors should explain why a power-law fit (note that it is not "exponential" as stated on page 10, line 3) should be adopted for the regression analysis in Figs. 7E-v,vi (a useful reference may be Joseph et al. eLife 2019: 10.7554/eLife.45077).

We thank the reviewer for the useful reference and the careless mislabeling of regression curve used. This figure has been redone and a linear regression is instead used that does not attempt to imply any physical law for a power or exponential fitting.

Change made: Fig. 7C

Minor comments:

1. The state of art of cell-resolved blood flow models employed to simulate microcirculatory hemodynamics is not accurately described in the introduction (page 4). More recent works should be cited and critically reviewed to present a fair view on the novelty of the computational model developed herein.

We apologize that the models were mentioned in a passing manner. However ,the need for brevity in introduction somewhat limits their expansion. We have instead gave more direct discussion on similar studies and their relevance to our present work in the Discussion section:

Page 14, lines 13 to 31

It is unclear what "realistic representation of local topologies in the network" (page 7, lines 28-31) means as a claim of novelty. If it means vessel "diameter variation", this geometric feature has been modeled by the works the author referenced (namely Roustaei et al. 2022, Zhou et al. 2021). If it means something else, for example, unsmooth or non-circular vessel surface (or "irregularity of the local endothelium surface" as mentioned on page 5, line 2), then strangely the effects of such features are actually not described in the manuscript.

We apologize for not meeting the expectation of novelty as claimed. We see value in the SGM study matrix have now generated data on three SGM scenarios. The SGM1 in the revised manuscript matches WT network impedance in the ISVs by including both axial variation in lumen diameter of the WT network and the elliptical fit representation of cross-sectional skewness seen in WT ISV lumens. SGM 2 has representation of axial variation but not luminal skewness and SGM3 has only geometric average similarity to WT ISVs. Essentially the comparison between SGM1 and SGM2 highlights the role of luminal cross-sectional shape skewness while SGM2 to SGM3 highlights the role of axial variation in luminal diameter. With this new SGM data set, we think we can better qualify the aspiration of demonstrating how vessel shape “irregularities” can alter network hemodynamics. The new findings and discussion can be found in the revised manuscript here:

Page 8, line 19 to page 9 line 36.

Why should Fig. 8 contain data from Marcksl1KO model 2? The scenario underlying model 2 was rejected earlier in the manuscript (see point 6 above), and the Marcksl1KO model 2 data are not mentioned in the text when describing the results of Fig. 8, either.

We have reanalyzed the experiment trend and rewritten the outcome of this results section. In summary, both models 1 and model 2 meet the trend of flow rate reduction (with respect to WT levels) in the CA observed in the experiment. Hence, model 2 inclusion is relevant to the WSS analysis. The changes pertaining to this can be found here:

Page 11, line 9 to page 13 line 10.

It is a dense article with loads of data, which is an advantage but only if appropriately streamlined. More subheadings should be considered, especially for section 2.3 (for which the current subsections appear mistaken, 2.3.1 followed by 2.4.2) The manuscript could also benefit from restructuring through optimal combination of simulation visualizations and quantitative analyses. For example, in Fig. 6, not all simulation snapshots are needed here (it is difficult to visually compare the changes between different cases), whereas some quantification in the form of histograms or boxplots will be handy for the readers to note the variation of WSS magnitudes and ranges.

Thank you for the advice, we removed the unnecessary graphical plots and refer to simulation videos in supplementary data instead for such cases. The bad indexing of results subsections has been fixed, while new subsections have been made for better directional narrative to the paper. These changes are colored in red throughout the revised results section:

Page 4, line 37 to page 13 line 39

Related to point 8, the authors could also consider integrating or synthesizing the analyses for individual aISVs and vISVs presented in various figures. Current descriptions for the ISV data appear scattered with frequent exceptions to the summarized trends or relationships. Some minor formatting issues should also be addressed, e.g. the confusing color codes in Figs. 9D-i, E-i.

Thank you for the advice, we have now pooled aISVs together into one group and vISVs into another, instead of discussing data trends on each of the 10 ISVs.

The mispattening case presented in the end of the results section (section "2.4.2") is interesting but appears loosely connected to the preceding contents. Also, it seems not even mentioned in the discussion section.

We agree that the mispatterning case has been only tangentially relevant to the rest of the manuscript. We have linked the topic thematically by network alterations transforming network flows. It is also now included in the discussion section here:

Page 15, lines 30 to 34

Finally, apart from the effect of topological features on local blood flow, the authors should consider the global flow redistribution arising from the network structure (useful refs. Include Chang et al. PLOS Computational Biology 2017: 10.1371/journal.pcbi.1005892; Meigel et al. Physical Review Letters 2019: 10.1103/PhysRevLett.123.228103; Schmid et al. eLife 2021: 10.7554/eLife.60208).

Thank you for the additional references. These are solid pieces of work that have been added to the discussion here:

Page 16, lines 3 to 10

**Referees cross-commenting**

This review report resonates with mine from an experimental perspective and I agree with all points made regarding issues of the current manuscript that the authors need to address with a revised version.

Reviewer #2 (Significance (Required)):

Significance: The particular merit of the work lies in its comprehensiveness of design and abundance of data, which will be of great interest to both the computational and experimental communities in this research field. However, some crucial details (especially with respect to the modelling aspects) are missing, thus hampering the scientific rigor and potential impact of the work. Furthermore, certain justifying statements appear speculative and inconclusive to explain the obtained data, especially regarding the effect of boundary conditions and systemic parameters. The citation of references (some not cited, some cited already but not properly discussed) also needs to be enhanced with engaging discussions to better bridge the findings of the current work (e.g. RBC partitioning in vascular network, effect of WSS on vasculature morphogenesis) with recent works on this research topic.

References

Fedosov DA, Caswell B, Karniadakis GE. 2010. A Multiscale Red Blood Cell Model with Accurate Mechanics, Rheology, and Dynamics. Biophys J 98:2215–2225. doi:10.1016/j.bpj.2010.02.002

Freund JB, Goetz JG, Hill KL, Vermot J. 2012. Fluid flows and forces in development: functions, features and biophysical principles. Dev Camb Engl 139:1229–45. doi:10.1242/dev.073593

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

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Referee #1

Evidence, reproducibility and clarity

The manuscript presents a detailed numerical model of blood flow in a region of the zebrafish vasculature.

The results section is quite intense and detailed. it is difficult to understand what the authors are after. I think a rewrite would beneficial. The authors present simulations for a wild type and a couple of phenotypes. For each of these they speculate on the possible adaptation mechanism leading to the discussed phenotype, as preservation of constant wall shear stress. However, the comparison between experiments and numerical simulations is really elusive as the conclusions on those mechanisms. Overall we suggest a rewrite with clearer organisation in a way that the reader is not overflown with useless details.

It is not always clear what info of the experiments are used in the simulations on top of the anatomy. Our understanding is that the pressure boundary conditions are set to match the red blood cel velocity observed in experiments. Is this always the case for the three phenotypes and which vessels ? There are about 7 inlets and outlets where to impose pressure boundary conditions. Can the author comment on the uniqueness of this problem? Can different combination of pressure boundary condition leading to the same result ? In how many points/vessels is the measured velocity matched ?

The argument that similar beating frequency in the WT and GATA1 MO suggest pressure does not change is not clear. If the heart was a volumetric pump it would impose the same flow rate, not the same pressure. It would be more useful to measure the cardiac output in terms of flow rate in the Dorsal Aorta. Previous measurements by Vermot suggested the latter would not change much in gata1 MO. It could be that the cardiac output is the same but the vasculature network is different in a way that the shear stress remain the same. It does not look like this was checked by the authors.

Additionaly, it would be useful to provide an effective viscosity for the different vessels, and an effective hydraulic impedance relating DP and Q to interpret the results.

Is the hydraulic impedance of the vessels kept constant in the smooth-geometry model? This needs clarification

As mentioned by the authors they propose a very complex and time expensive simulation. However the results they report are kind of intuitive. Given the availability of the experimental results, would it be useful to use a simpler red blood cell model in the future, to make their simulation more practical? Or clarify when such demanding simulations can add something new?

The authors should check their references as this is not the first time work has been done on the topic. Would be good to have a check in the work of Freund JB and colleagues, as well as Dickinson and colleagues and Franco and colleagues to discuss how the work compares. There may be interesting work in modelling cardiac flow forces in the embryo too.

Significance

The authors discuss the applicability of a detailed numerical model of blood flow in a region of the zebrafish vasculature.

We are not expert in the lattice boltzmann method used here, but the results are what it would be expected from a physical stand point, and together with the information from the method section, we do not have major concerns about the numerics.

Author Response:

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

We would like to thank all Reviewers for their careful evaluation of our work. Below please find our responses and comments.

Reviewer #1 (Recommendations For The Authors):

1) The detection of cell-released GLP-1 is addressed in an indirect, averaged way in Fig. 2 - Supplement 1. This question seems like a good opportunity for an antagonist experiment (Exendin-9), which presumably would require much lower concentrations than those used to antagonize a saturating dose of GLP-1. It would also be much more convincing if GLPLight1 could be used to detect stimulated release of GLP-1 from the GLUTag cells.

We tried multiple times to acutely stimulate GLUTag cells using Forskolin and IBMX, but unfortunately we did not observe any robust fluorescence increase of GLPLight1. The only observation that was consistent was the higher baseline fluorescence of GLPLight1, and the reduced maximal response to saturating GLP-1 when GLPLight1 expressing HEK cells were cultured overnight with GLUTag cells. We considered this assay to be at best qualitative and — despite the aforementioned attempts — could not determine quantitative values.

2) The excitation-ratiometric response of the sensor, shown in Fig. 1D, is usually accompanied by strong pH-dependence of sensor function. It would be valuable to characterize this pH-dependence, using permeabilized cells in which the pH is changed; the ability of small (0.2-0.5 unit) pH changes to produce changes in fluorescence, as well as to affect the dynamic range of the sensor, should be characterized. This will prevent the misidentification of agents that affect cellular pH as having (for instance) an inhibitory effect on the binding of GLP-1 to GLPLight.

The pH sensitivity of cpGFP-based sensors is a valid concern. However, considering that the cpGFP module from GLPLight1 is intracellular (and thus largely protected from potential extracellular pH changes) we assume that GLPLight1 signal should be robust in most in-vivo or cell-based assays. In fact we have previously characterized this for a similarly-built neuropeptide sensor (PMID: 35145320) and believe that this will be the case also for GLPLight1.

3) The reported Kd for Exendin-9 is in the low nM range. Please explain the partial response at 1000x the concentration (including a discussion of the Kd of GLP-1 itself, as well as its off kinetics, and a comparison of this assay to the assays used previously).

The partial response is due to the presence of 1 uM GLP-1 in the imaging buffer, which is in constant competition with Exendin-9 for the binding to GLPLight1. Because GLP-1 has similar affinity as Exendin9 (see for example PMIDs: 34351033 and 21210113) and both are present at saturating concentration, we did expect to observe a partial response from GLPLight1. In this study, we did not exactly determine the on and off kinetics of both GLP-1 and Exendin9 on the GLPLight1 sensor due to technical challenges: to perform these experiments, we would need to set up a perfusion system where we could remove the unbound ligand and either wash off the bound ligand with buffer or compete it out with an antagonist. Unfortunately, we currently do not have access to such a set up.

4) Are the turn-on kinetics in Fig. 2C limited by drug application or by association? Are the on-rates much slower for the lower concentrations used for Fig. 2C? This is important for knowing how fast responses are likely to be at the lower concentrations likely to be achieved by endogenous release.

If we consider Fig 2B and 2C, we assumed the on-kinetics to be mostly driven by association since the ligand is expected to be homogeneously distributed.

The on-rate kinetics are indeed slower when lower concentrations of GLP-1 are used as shown in (Figure 2b) where we observe a TauOn of 4.7s with 10 uM GLP-1 and much slower kinetics when GLP-1 is applied a 1 uM for example (Figure 3d). As a result, we chose to incubate the ligand with GLPLight1 expressing cells for at least 30 minutes before the measurement of the dose-response to be close to equilibrium.

5) The parameters for the fitted dose-response curves in Fig 2C should be listed. The ~4x discrepancy between the dose-response in HEK-293 cells and neurons should be discussed. Are there known auxiliary subunits, dimerization, or lipid dependence that might account for this? It seems important to understand this if the sensors are to be used in an assay that may compare different systems.

We added the EC50 values to Fig 2C as requested. We did not consider a 4x discrepancy to be significant, because the measurement error in the EC50 region is relatively high and this difference seemed to be within the error range. In fact, the 95% confidence interval ranges are 7.8 to 11.1 nM in Neurons and 23.8 to 32.1 nM for HEK cells, if we consider the upper and lower boundaries of each, the difference drops to around 1-fold. We also performed a statistical test to compare the two fits (Extra sum of squares F-test) that confirmed the two fits were not significantly different (P value = 0.3736). Of course, the interaction partners and membrane composition are different in HEK cells and neurons and probably have an influence on the EC50 of GLPLight1, but their exact influence is unclear.

6) It seems surprising that removal of the endogenous N-terminal secretory sequence is actually helpful for membrane expression. Do the authors have any suggested explanation for this?

GLPLight1 contains an N-terminal hemagglutinin (HA) secretory motif. The hmGLP1R sequence that we chose also contained an endogenous secretory sequence that most likely interfered with the membrane transport mechanism and resulted in a lower sensor expression with both secretory sequences. We thus decided to keep the HA instead of endogenous to remain consistent with other sensors created in-house.

7) In Fig. 1, supplement 3, are the transient responses real? Do they occur with the control construct?

While we have not measured the G-protein recruitment on GLPLight-ctr, we have often observed this phenomenon for various receptors and ligands. The transient responses are thus most likely an artifact after manual addition of the ligand possibly due to:

-       Temperature difference

-       Exposure of the plate to ambient light before resuming measurement (phosphorescence)

-       Re-suspension of the cells affecting the proximity to the detector

-       Other unknown variables

If these responses were real, we would also expect them to be more sustained over time.

8) Please include a sentence or two explaining the luminescence complementation assay, and a reference.

We updated the results section of the manuscript with a section describing the luminescence complementation assay along with a reference:

“Next, we compared the coupling of GLPLight1 and its parent receptor (WT GLP1R) to downstream signaling. We first measured the agonist-induced membrane recruitment of cytosolic mini-G proteins and β-arrestin-2 using a split nanoluciferase complementation assay (Dixon et al., 2016). In this assay both the sensor/receptor and the mini-G proteins contains part of a functional luciferase (smBit on the sensor/receptor and LgBit for Mini-G proteins) that becomes active only when these two partners are in close proximity (Wan et al., 2018).”

Bravo to the authors for already making the sensor plasmids available at addgene.com. It would be helpful to include the plasmid IDs and/or a URL in the manuscript.

We would like to thank Reviewer #1 for noticing this. We have updated the data availability section of the manuscript and added the AddGene plasmid numbers of the constructs generated in this study.

Reviewer #2 (Recommendations For The Authors):

1) There are some parts of the introduction that need clarification. For example, GLP1 is quoted as an anorexigenic peptide, however, that is probably only true for centrally- derived GLP1. There is no evidence that enteroendocrine-derived GLP1 (the major pool) is anorexigenic- it is likely to be substantially degraded by DPPIV before reaching the brain. In any case, the discovery of GLP1 was always one of glucose-dependent insulin secretion, with the brain system being described decades later. Overall, the intro needs to be slightly reframed. While the tools presented here are more useful for assessment of central GLP1-releasing circuitry, they are ultimately based upon GLP1R signaling that is much better validated in the periphery.

We have slightly reframed the introduction accordingly.

2) "The human GLP1R (hmGLP1R) is a prime target for drug screening and drug development efforts, since GLP-1 receptor agonists (GLP1RAs) are among the most effective and widely-used weight-loss drugs available to date (Shah and Vella, 2014)." GLP1R was for two decades the breakthrough drug for treatment of type 2 diabetes mellitus and correction of glucose tolerance as assessed through HbA1c. It is only through reporting on millions of patients receiving GLP1RA that the weight loss effects were noted, leading to Phase1-3 trials and eventual approval for obesity indication. Again, some slight reframing of the introduction is required here.

Also for this point, we have slightly reframed the introduction accordingly.

3) GLP1 was applied at a maximal dose of 10 uM, which is 10-fold higher than maximal. Can the authors confirm absence of cytotoxic effects of exposing to peptide at such concentration? Ex4 (9-39) at such concentrations is usually cytotoxic at least in primary tissue.

We did not observe any obvious cytotoxic effect of GLP-1 at this concentration in HEK293T cells or Neurons.

4) "As expected, GLPLight1 responded to both GLP1RAs with almost maximal activation, on par with GLP1 (Figure 2a)." Such a claim is difficult to interpret without concentration-response curves, since the maximal concentration of liraglutide and semaglutide might not have been achieved in these experiments.

We agree with this statement is difficult to interpret without further clarification. We know from the literature that GLP-1, liraglutide and semaglutide all have very high affinity to the hmGLP1R (PMID: 31031702). We also proved that GLPLight signal saturates at concentrations above 1 uM of GLP-1 (figure 2C), we thus applied a 10x excess of all ligands and considered this signal as maximal.

5) "These results indicate that GLPLight1 can serve as a direct readout of pharmacological drug action on the hmGLP1R with higher temporal resolution than previously available approaches, such as downstream signaling assays (Zhang et al., 2020)." Many investigators use cAMP imaging to investigate GLP1R signaling, which is arguably of similar spatiotemporal resolution, also with the advantage of FRET quantification in some cases (e.g. EpacVV). Direct GLP1R signaling can also be inferred using cell lines heterologously-expressing GLP1R. Thus, the advantage of the current probes is that they can be used to readout direct GLP1R activation in native cells/tissues where promiscuous class B binding might limit signaling measures or where endogenous GLP1 release needs to be investigated.

We have edited the manuscript text accordingly.

6) "State-of-the-art techniques for detecting endogenous GLP-1 or glucagon release in vitro from cultured cells or tissues consist of costly and time-consuming antibody- based assays (Kuhre et al., 2016) or analytical chemistry procedures (Amao et al., 2015)." Agreed, but non-specificity/cross-reactivity of such assays is more prohibitive/problematic (e.g. against glicentin).

We have edited the introduction accordingly.

7) The studies using co-culture of GLUTag and GLP1Light1-HEK293 cells, whilst interesting, are not entirely convincing in their current form. Firstly, co-culture could influence GLP1Light expression levels (can the authors label FLAG?). Secondly, specificity of the response is not tested e.g. by adding Ex4 (9-39). Thirdly, titration with GLUTag conditioned media is not performed.

We partially addressed this issue in the answer to comment #1 from Reviewer #1. We previously performed a FLAG staining of GLPLight1 in the presence or absence of GLUTag cells and we did not notice any obvious difference. This goes in line with the fact that GLPLight1 is signaling inert, and the presence of GLP1 should not interfere with the surface expression of the sensor. We also checked that HEK293T cells did not express high levels of GLP1R according to the BioGPSCell line Gene Expression profile (https://maayanlab.cloud/Harmonizome/gene_set/HEK293/BioGPS+Cell+Line+Gene+Expression+Profiles).

We also tried to add GLUTag media after stimulation in bolus to GLPLight1 expressing cells and observed no response. This indicated that the “sniffer” cells must be present in close proximity to GLUTag cells for an extended period of time to observe any substantial difference in response, justifying our choice of experimental setup.

8) "Given that our photocage was placed at the very N-terminus of photo-GLP1, our results show that this caging approach prevents the peptide's ability to activate GLP1R but, at the same time, preserves its ability to interact with the ECD." An alternative hypothesis is that PhotoGLP1 does activate GLP1R, but this is undetectable with the sensitivity of GLP1Light. PhotoGLP1 cAMP concentration-response assays are needed (uncaged versus cage) to properly characterize and validate the compound (as would be standard for any newly-described GLP1R peptide ligand).

While we agree that there is a chance that Photo-GLP1 could activate GLP1R at high concentrations, we think that the characterization of Photo-GLP1 has to be determined by the end user directly with the technique of choice (GLPLight1 in our case) in order to get a reliable comparison of potency and efficacy. We modified the text accordingly to more accurately reflect the direct conclusions from our data, as follows:

“our results show that this caging approach prevents the peptide's ability to activate GLPLight1”.

9) "Surprisingly, GLPLight1 shows a fluorescent response in all three uncaged areas, while its fluorescence remained unaltered throughout the rest of the FOV, indicating high spatial localization of the response to GLP-1 (Figure 3f)." Why is this surprising?

We agree that this result is, indeed, not surprising and would like to thank Reviewer #2 for spotting this mistake, which has now been corrected in the manuscript.

10) The localized PhotoGLP1 experiments are interesting and show the utility of the ligand. There is however activation outside of the region of uncaging, which would argue against a pre-bound ECD mode of action. Possibly some PhotoGLP1 is pre- bound to the ECD, and some is freely diffusing? Alternatively, the scan area might be below the diffraction limit/accuracy of the microscope?

We would like to thank Reviewer #2 for this comment and agree with their observation. There could be some free Photo-GLP1 that gets photo-activated and binds regions around the uncaging area (similar to what has been observed for Photo-OXB:,PMID: 36481097). The activation around the uncaging area could also be due to lateral diffusion of the activated receptor on the membrane. There is also most likely some light diffraction at the uncaging area that could account for this phenomenon. To increase the spatial resolution, future studies could involve uncaging during sensor imaging via two-photon microscopy.

11) What was the rationale for caging native GLP1, which is then susceptible to DPPIV-mediated degradation? Would the N-terminal cage and first 2 amino acids also not be cleaved by DPPIV, thus rendering the tool of limited in vivo application? Conversely, PhotoGLP1 provides a template for similar light-activated (stabilized) GLP1R agonists such as Ex4 or liraglutide.

Thank you for making us aware of this (in vivo) limitation. We designed photoGLP1 as a tool for neurobiological experiments in the brain, where DPPIV expression would be low compared to peripheral organs (https://www.proteinatlas.org/ENSG00000197635-DPP4/tissue). We also envisage that the presence of the photocage would be enough to hinder the binding to DPP4 that cuts the first 2 AA. This hypothesis, however, was never tested experimentally, and we, therefore, acknowledge the limitation in the manuscript. We would furthermore like to thank the reviewers for his comment on additional photo-caged GLP1 agonists, which could be developed future studies.

12) It wasn't clear how GLP1Light could be used as a HTS screen for drug discovery? Surely, conventional systems (e.g. GLP1R + BAR/Ca2+/cAMP reporting) allow signal bias, an important component of GLP1RA action, to be assessed. Or could GLP1Light1 be used as a pre-screen to exclude any ligands that do not orthosterically bind GLP1R?

We would like to thank Reviewer #2 for this comment and would like to offer some clarification. We indeed thought that GLPLight1 could be used as a first line of screening to exclude ligands that do not bind in the orthosteric pocket. It is also a rather flexible method as the fluorescence increase of those sensors can be monitored using various techniques/devices that are available in most labs (e.g. microscopy, plate reader, flow cytometry).

13) Limitations of GLP1Light1 and PhotoGLP1 are not acknowledged in the discussion.

We would like to thank Reviewer #2 for pointing out the lack of description of the limitations of these tools, which have now been added to the Discussion.

14) Full characterization of PhotoGLP1 is missing, to include UV/Vis, Tr and HRMS.

PhotoGLP1 was fully characterized by UV/Vis and HRMS, and all experimental and analytical data was uploaded as supplementary data when the manuscript was initially submitted for publication in eLife.

Reviewer #3 (Recommendations For The Authors):

1) The ~1000 fold lower EC50 for GLP1 of GLPLight1 compared with native GLP1R needs to be openly acknowledged as a major limitation of the sensor, as this will substantially reduce the types of experiment for which it will be useful. Because it needs 1000 times higher GLP1 levels than wild type GLP1R to be activated, it is unlikely, for example, to be useful for monitoring the dynamics of activation of native GLP1R in vivo. The claim that the sensor could be used for in vivo imaging for fibre photometry is therefore an exaggeration.

We would like to first thank Reviewer #3 for this comment and to further provide some clarification. We recognized that the data presented in this manuscript might have been confusing when comparing the affinity of GLP1R (using cAMP) and GLPLight1 (using the fluorescence increase because there is no coupling to cAMP). We believe that the low EC50 measured in the cAMP assay cannot accurately be compared to GLPLight1 response because it is an enzymatically amplified process. In order to support this claim, we included another set of experiments where we titrated agonist- induced recruitment of miniGs protein to the GLP1R receptor and found an EC50 of 3.8 nM for native GLP-1 using this assay (added as panel l in Figure1 Supplement 3). We thus confirmed that the nature of the assay itself has a drastic influence on the EC50 measured and it is not unusual to observe 100x fold difference of EC50 for the same receptor-ligand pair.

We believe that the miniGs protein recruitment is a better comparison to GLPLight1 because it is not enzymatically amplified. This assay reveals that GLPLight1 has around 8-fold lower affinity to GLP1 compared to its parent receptor, which is in line with the EC50 loss observed previously for other GPCR-based sensors of this class. We are thus confident that GLPLight1 has to potential to be used in vivo under specific circumstances, specifically in brain tissue. We elaborated on this point in the Discussion part of the manuscript.

2) Fig2 suppl 1 is described as demonstrating a reduced response of GLPLight1 to GLP-1 when HEK cells with were cultured with GLUTag cells. However, it is speculation to conclude that this is because GLP1Light1 was partially pre-activated by endogenous GLP-1, without demonstrating the response of GLPLight1 before and after GLUTag cell stimulation. Unless additional data are generated, the presented data do not convincingly demonstrate that GLP1Light1 can detect GLP1 released from GLUTag cells.

We would like to thank Reviewer #3 for this comment which has been addressed already in the replies to Comment#1 from Reviewer #1 and Reviewer #2.

3) The authors should openly acknowledge that photo-uncaging the GLP1 probe might not be very helpful for monitoring the temporal dynamics of the GLP1-GLP1R interaction, because unless all the photocaged glp1 is released by the light stimulus, the activation of photo-released GLP1 will be slowed by the remaining caged GLP1, and the dynamics will be slower than for native GLP1. This makes it unsuitable for many temporal questions, although it might be useful to deliver GLP1 in a spatial restricted manner.

We do agree that the biggest advantage of Photo-GLP1 is its ability to be activated in a very localized manner. We also agree that the presence of caged Photo-GLP1 will influence the binding of the uncaged GLP-1. Nevertheless, there is still an advantage of using Photo-GLP1 in some assays such as pharmacological activation on brain slices. In fact, we have shown for our Photo-OXB molecule that the perfusion of OXB was much slower at eliciting neuronal depolarization compared to uncaging of Photo- OXB (see PMID: 36481097). We think that this was mainly due to the slow diffusion kinetics of the peptide into the brain tissue. We also think that uncaging can provide a more controlled activation with varying laser power and uncaging duration.

4) To claim (as currently in the discussion) that GLPLight1 has potential to be used for investigating the dynamics of endogenous GLP1, the authors would need to compare the dynamics of the GLP1Light sensor with wild type GLP1R. We do not know that its activation dynamics will reproduce native glp1r.

We would like to thank Reviewer #3 for this comment and would like to offer some clarification. Since GLPLight1 does not couple to intracellular signaling, it was impossible to compare its activation kinetics to GLP1R WT using the same assay. However, we can offer a relative comparison since we know that GLPLight1 takes around 50 seconds to be activated using 1 µM GLP-1 (figure 2B) and that it takes a similar time for GLP1R to be activated in the miniG protein recruitment assay (Fig 1 Supplement 3) using 100 nM GLP-1. Considering that GLPLight1 has a lower affinity than the GLP1R (8-10x lower), we think that the activation kinetics of both the sensor and GLP1R are comparable.

Additional comments:

1) In fig 2A,B, it is not clear whether the trace shows a partial reversal of GLP1- triggered activation by Ex9, or Ex9-independent receptor desensitization. A control trace is required to show the kinetics of GLP1-triggered activation without the addition of Ex9.

We would like to thank Reviewer #3 for this comment. We can exclude the possibility of Ex9-independent desensitization because GLPLight1 has been shown to be signaling inert to all G-proteins, Beta arrestin-2 and cAMP. Moreover, we have observed that the fluorescence signal was stable for more than 30 minutes for the GLP-1 titrations, even at high concentrations of ligand.

2) It would be helpful if the pEC50 for WT GLP1 were also shown in table 1, for comparison with the GLP1 mutants.

We would like to thank Reviewer #3 for this comment, and we have now added the respective pEC50 for WT GLP1 to Table 1.

3) Fig2 suppl 1. The methods and analysis for this figure are inadequately explained. To show that the HEK-GLPLight1 cells are responding to GLP1 released from GLUTag cells, the GLPLight1 response needs to be shown before and after GLUTag cell stimulation with an agent that should trigger GLP-1 release.

We would like to thank Reviewer #3 for this comment which has been partially addressed already in the replies to Comment#1 from Reviewer #1 and Reviewer #2.

Since we did not observe any response to acute stimulation of GLUTag cells we considered the high glucose concentration present in the culture media being a stimulation agent for GLUTag cells, which has been previously reported (PMID: 17643200).

4) Fig 3g and others: The end of the photo activation period needs to be represented correctly on the timeline. In 3g, the bar that should indicate when photoactivation was applied does not end at the zero time point (which is labelled as the time relative to photoactivation).

We would like to thank Reviewer #3 for pointing this out. The shaded area representing the photo-activation has been matched accordingly.

5) Discussion para 1: the authors claim their data show that ligand induced activation of human GLP1R occurs more slowly than others similar GPCR sensors - they should give actual data to substantiate this claim, since the time course of glp1r activation has not been analysed and compared with other sensors in the manuscript.

We added data to support this claim to the discussion: “As a reference, other previously-characterized class-A GPCR-based neuropeptide biosensors showed sub- second activation kinetics (Duffet et al., 2022a; Ino et al., 2022).”

6) Methods: what wavelength was used for recording emission from GLP1Light1? The excitation wavelength is given, but I can't see the emission wavelength(s). In fig 1d, the excitation and emission spectra should be depicted in different colours/line properties, otherwise this figure is very confusing.

We updated figure1d and changed the colors to improve data visualization. Regarding the missing wavelength, we would like to clarify that both wavelengths were already described in the methods section as: “The excitation and emission spectra were measured at λem =560nm and λex\= 470nm, respectively, on a TECAN M200 Pro plate reader at 37 °C. “. We would be happy to rewrite this paragraph, if necessary, shall it remain unclear to the reader.

I think there is definitely an interesting point to be made if we should restrict certain parts of free-speech. Do we get rid of hate-speech and spam even when they are harmful? Does that contradict democracy or uphold it? I don't know that I can answer these questions as online free-speech would set precedent to a slew of things (online +in person) and requires much more knowledge than I can provide as a freshman in college lol.

Author Response:

Reviewer #1 (Public Review):

This manuscript features a key technical advance in single-molecular force spectroscopy. The critical advance is to employ a click chemistry (DBCO-cycloaddition) for making a stable covalent connection between a target biomacromolecule and solid support in place of conventional antigen-antibody binding. This tweak dramatically improves the mechanical stability of the pulling system such that the pulling/relaxation can be repeated up to a thousand times (the previous limit was a few hundred cycles at best). This improvement is broadly applicable to various molecular interactions and other types of single-molecule force spectroscopy allowing for more statistically reliable force measurements. Another strength of this method is that all conjugation steps are chemically orthogonal (except for Spy-catcher conjugation to the termini of a target molecule) such that the probability of side reactions could be reduced.

The reliability of kinetic and thermodynamic parameters obtained from single-molecule force spectroscopy depends on statistics, that is, the number of pulling measurements and their distribution. By extending the number of measurements, this robust method enables fundamental/critical statistical assessment of those parameters. That is, it is an important and interesting lesson from this study that ~200 repeats can yield statistically reasonable parameters.

The authors carried out carefully designed optimization steps and inform readers of the critical aspects of each. The merit, quality, and rigor as a method-oriented manuscript are impressive. Overall, this is an excellent study.

We appreciate for the positive evaluation for our work. Additionally, the minor suggestions were helpful to improve our manuscript. Thank you!

Reviewer #2 (Public Review):

In this study, the authors have developed methods that allow for repeatedly unfolding and refolding a membrane protein using a magnetic tweezers setup. The goal is to extend the lifespan of the single-molecule construct and gather more data from the same tether under force. This is achieved through the use of a metal-free DBCO-azide click reaction that covalently attaches a DNA handle to a superparamagnetic bead, a traptavdin-dual biotin linkage that provides a strong connection between another DNA handle and the coverslip surface, and SpyTag-SpyCatcher association for covalent connection of the membrane protein to the two DNA handles.

The method may offer a long lifetime for single-molecule linkage; however, it does not represent a significant technological advancement. These reactions are commonly used in the field of single-molecule manipulation studies. The use of multiple tags including biotin and digoxygenin to enhance the connection's mechanical stability has already been explored in previous DNA mechanics studies by multiple research labs. Additionally, conducting single-molecule manipulation experiments on a single DNA or protein tether for an extended period of time (hours or even days) has been documented by several research groups.

One of the unique features of our work is the development of a robust single-molecule tweezer method that is applicable to membrane proteins, rather than simply making another stable system. As re-written in Introduction, it is not straightforward as we have to consider the membrane reconstitution. We believe that our work is expected to overcome the bottleneck in membrane protein studies that arises when using single-molecule tweezer methods.

To improve the delivery of the contextual information, we revised Introduction, Results, and Discussion. The first four paragraphs in the Introduction briefly review previous tweezer methods with an improved stability and delineate where our work is placed. In the first paragraph of the Results, we also briefly discussed how and why our DBCO tethering strategy differs from previous DBCO methods. In the first paragraph of the Discussion, we compared the previous methods regarding the stability improvement.

Additionally, the revised manuscript now includes new findings – the full dissection of structural transitions of a helical membrane protein, the observation of hidden helix-coil transitions at a constant force, and the estimation of kinetic pre-exponential factors. We believe that the new findings provide important insights into membrane protein folding, in addition to the usefulness of our method itself for membrane protein studies. We extensively edited the main text and Methods accordingly. Relevant figures are Figures 6 and 7, Figure 6–figure supplements 1–3, and Figure 7–source data 1.

Reviewer #3 (Public Review):

The authors describe a method to tether proteins via DNA linkers in magnetic tweezers and apply it to a model membrane protein. The main novelty appears to be the use of DBCO click chemistry to covalently couple to the magnetic bead, which creates stable tethers for which the authors report up to >1000 force-extension cycles. Novel and stable attachment strategies are indeed important for force spectroscopy measurements, in particular for membrane proteins that are harder and therefore less studied in this regard than soluble proteins, and recording >1000 stretch and release cycles is an impressive achievement. Unfortunately, I feel that the current work falls short in some regards to exploring the full potential of the method, or at least does not provide sufficient information to fully assess the performance of the new method. Specific questions and points of attention are included below.

We appreciate for the positive evaluation. We were able to largely improve our manuscript while preparing our responses to the comments. Thank you!

- The main improvement appears to be the more stable and robust tethering approach, compared to previous methods. However, the stability is hard to evaluate from the data provided. The much more common way to test stability in the tweezers is to report lifetimes at constant force(s). Also, there are actually previous methods that report on covalent attachment, even working using DBCO. These papers should be compared.

As shown in Figure 4E, we evaluated the robustness of our method in a way suggested by you – the lifetime measurement at a constant force. Specifically, ~12 hours at 50 pN. Definitely, our tweezer approach established here is the most robust method for membrane protein studies. Please refer to the section “Assessing robustness of our single-molecule tweezers” in page 7 and line 31.

We discussed the previous covalent methods for which quantitative data are presented in light of the system stability. Please refer to the first paragraph of Discussion. We also briefly discussed how and why our DBCO tethering strategy differs from previous DBCO methods, in the first paragraph of Results.

- The authors use the attachment to the surface via two biotin-traptavidin linkages. How does the stability of this (double) bond compare to using a single biotin? Engineered streptavidin versions have been studied previously in the magnetic tweezers, again reporting lifetimes under constant force, which appears to be a relevant point of comparison.

The papers in this comment showed that the tethering lifetimes of biotin-streptavidin variants were affected by the asymmetric bead anchoring point. However, the situation does not apply to our work as we do not anchor traptavidin to beads. Besides, the stability comparison between the single- and double-biotin systems is not the main point of our work, so we do not have the answer to the question. However, we cited the reference in the first paragraph of Discussion where we discuss the system stability.

- Very long measurements of protein unfolding and refolding have been reported previously. Here, too, a comparison would be relevant.

We briefly discussed the relevant previous works in the first paragraph of Discussion.

In light of this previous work, the statement in the abstract "However, the weak molecular tethers used in the tweezers limit a long time, repetitive mechanical manipulation because of their force-induced bond breakage" seems a little dubious. I do not doubt that there is a need for new and better attachment chemistries, but I think it is important to be clear about what has been done already.

The sentence is in Abstract, so we also had to consider the conciseness. By simply adding the phrase “used for the membrane protein studies”, we can place our work into a more proper context.

In page 2 and line 3, “…However, the weak molecular tethers used for the membrane protein studies have limited long-time, repetitive molecular transitions due to force-induced bond breakage…”

- Page 5, line 99: If the PEG layer prevents any sticking of beads, how do the authors attach reference beads, which are typically used in magnetic tweezers to subtract drift?

The PEG layer consists of biotin-PEG and methyl-PEG at a 1:27.5 molar ratio. As the reference beads are coated with streptavidin, they are attached to the PEG layer by the regular biotin-streptavidin interaction. In page 19 and line 7, you can refer to “…The polystyrene beads are attached to the PEG surface via biotin-streptavidin interaction. The beads are used as reference beads for the correction of microscope stage drifts…”

- Figure 3 left me somewhat puzzled. It appears to suggest that the "no detergent/lipid" condition actually works best, since it provides functional "single-molecule conjugation" for two different DBCO concentrations and two different DNA handles, unlike any other condition. But how can you have a membrane protein without any detergent or lipid? This seems hard to believe.

We explained the raised point in page 6 and line 18,

“…Indeed, the best condition was in the absence of any detergents or lipids (Figure 3; no detergents/lipids only during the conjugation step). This situation is possible because membrane proteins are sparsely tethered to the chamber surface, which kept them from aggregating. However, not using detergents or lipids means that the membrane proteins are definitely deformed from their native folds. Therefore, we sought an optimal solubilization condition for membrane proteins during the DBCO-azide conjugation step...”

Figure 3 also seems to imply that the bicelle conditions never work. The schematic in Figure 1 is then fairly misleading since it implies that bicelles also work.

The buffer conditions shown in Figure 3 are those ONLY during the DBCO-azide conjugation step. In this step, the bicelle conditions did not work. Therefore, after the conjugation in 0.5% DDM, the buffer was exchanged with a bicelle solution. This process is shown in Figure 2 and the finally assembled system is depicted in Figure 1.

To clarify this point, we put a note “Buffer conditions only during the DBCO-azide conjugation step” just above the buffer conditions in Figure 3. You can also find for the relevant exchange step in page 6 and line 31, “…Following a 1 h incubation of the beads in the single-molecule chamber at 25°C, unconjugated beads were washed, and the detergent micelles were exchanged with bicelles to reconstitute the lipid bilayer environment for membrane proteins…”

- When it comes to investigating the unfolding and refolding of scTMHC2, it would be nice to see some traces also at a constant force. As the authors state themselves: magnetic tweezers have the advantage that they "enable constant low-force measurements" (page 8, line 189). Why not use this advantage?<br /> In particular, I would be curious to see constant force traces in the "helix coil transition zone". Can steps in the unfolding landscape be identified? Are there intermediates?

Yes, please refer to Figure 6. We were able to dissect three distinct transitions from the fully unstructured state to the native state, including the helix-coil transitions. We also reconstructed the folding energy landscape using a deconvolution method.

Please refer to the pertinent sections in the main text, which are titled “Structural transitions and folding energy landscape over extended time scales” and “Mechanistic dissection of folding transitions”.

- Speaking of loading rates and forces: How were the forces calibrated? This seems to not be discussed.

We wrote an additional section in Methods titled “Instrumentation of single-molecule magnetic tweezers”, where we discuss the force calibration. For the actual force calibration data, please see Figure 4–figure supplement 1A.

In page 20 and line 10, “…The mechanical force applied to a bead-tethered molecule was calibrated as a function of the magnet position using the formula F = k_B_T∙L/δx_2 derived from the inverted pendulum model96, where _F is the applied force, k_B is the Boltzmann constant, _T is the absolute temperature, L is the extension, and _δx_2 is the magnitude of lateral fluctuations…”

And how were constant loading rates achieved? In Figure 4 it is stated that experiments are performed at "different pulling speeds". How is this possible? In AFM (and OT) one controls position and measures force. In MT, however, you set the force and the bead position is not directly controlled, so how is a given pulling speed ensured?<br /> It appears to me that the numbers indicated in Figures 4A and B are actually the speeds at which the magnets are moved. This is not "pulling speed" as it is usually defined in the AFM and OT literature. Even more confusing, moving the magnets at a constant speed, would NOT correspond to a constant loading rate (which seems to be suggested in Figure 4A), given that the relationship between magnet positions and force is non-linear (in fact, it is approximately exponential in the configuration shown schematically in Figure 1).

You are correct, so we simply modified the “pulling speed” to “magnet speed” in the figure caption. The loading rates provided in the figure (with the notation <>) were average loading rates in 1–50 pN to provide rough estimates. We actually specified it in the caption as “average force-loading rate”. However, this can be misleading at a glance, so we just deleted all the loading-rate values in the figure and caption.

- Finally, when it comes to the analysis of errors, I am again puzzled. For the M270 beads used in this work, the bead-to-bead variation in force is about 10%. However, it will be constant for a given bead throughout the experiment. I would expect the apparent unfolding force to exhibit fluctuations from cycle to cycle for a given bead (due to its intrinsically stochastic nature), but also some systematic trends in a bead-to-bead comparison since the actual force will be different (by 10% standard deviation) for different beads. Unfortunately, the authors average this effect away, by averaging over beads for each cycle (Figure 4). To me, it makes much more sense to average over the 1000 cycles for each bead and then compare. Not surprisingly, they find a larger error "with bead size error" than without it (Figure 5A). However, this information could likely be used (and the error corrected), if they would only first analyze the beads separately.

We might be wrong, but there seems to be a misunderstanding. First, we added Figure 5–figure supplement 1 where you can see individual traces. As expected, the levels of unfolding forces/sizes appear consistent during the progress of pulling cycles. Second, the advantage of averaging for different beads is that you can effectively remove the bead size effect. This “averaging-out” is the key strategy in our kinetic analysis. Based on the error estimation, if you average the values of kinetic parameters obtained from different beads, you can then estimate them with reasonably small errors despite the bead size variations. This becomes more evident after initial hundreds of pulling cycles. The errors for 200 and 1000 cycles are of only ~1% difference, indicating that you do not need to blindly run the pulling cycles. These results are based on the “averaging-out” strategy, which is the merit of our analysis. For more details, please see the section in the main text titled “Assessing statistical reliability of pulling-cycle experiments”, where relevant figures, figure supplements, and Method sections are referred.

What is the physical explanation of the first fast and then slow decay of the error (Figure 5B)? I would have expected the error for a given bead after N pulling cycles to decrease as 1/sqrt(N) since each cycle gives an independent measurement. Has this been tested?

If the sampling was from one population (here, unfolding probability profile), the error would follow a 1/√n decay as expected for the standard error. In our analysis, however, we estimated the expected “mean” errors, regardless of detailed shapes of the unfolding probability profiles. To this end, we sampled the data from different possible profiles (shown in Figure 5–figure supplement 5). We then averaged all the error plots to obtain the plot of the mean errors during progress of pulling cycles (black curve in Figure 5D). In this case, the plot does not have to follow the standard error curve represented by the factor 1/√n.

We tested this by fitting with the model function of y = A/√n, for various lower limit of N = 10, 30, 50, 100, 300, and 500 in the regression analysis (Figure 5–figure supplement 6). The results of the reduced chi-square (χ2) used for a goodness-of-fit test (χ2 = 1 for the best fit) indicates that the two-term exponential model (χ2 = 1.60) shows a better fit than the reciprocal square root model (χ2 = 2.30–6.01). The regression model adopted in our analysis is a phenomenological model that more properly describes the error decay curve. The trend of the first fast and then slow decay is not unusual because it is also expected for the reciprocal square root model – the plot 1/√n decays fast and then slowly, too (Figure 5–figure supplement 6).

Author Response

Reviewer #1 (Public Review):

Estimating the effects of mutations on the thermal stability of proteins is fundamentally important and also has practical importance, e.g, for engineering of stable proteins. Changes can be measured using calorimetric methods and values are reported as differences in free energy (dG) of the mutant compared to wt proteins, i.e., ddG. Values typically range between -1 kcal/mol through +7 kcal/mol. However, measurements are highly demanding. The manuscript introduces a novel deep learning approach to this end, which is similar in accuracy to ROSETTA-based estimates, but much faster, enabling proteomewide studies. To demonstrate this the authors apply it to over 1000 human proteins.

The main strength here is the novelty of the approach and the high speed of the computation. The main weakness is that the results are not compared to existing machine learning alternatives.

We thank Prof. Ben-Tal for taking the time to assess our work, and for his comments and suggestions below.

Reviewer 2 (Public Review):

Summary:

This work presents a new machine-learning method, RaSP, to predict changes in protein stability due to point mutations, measured by the change in folding free energy ΔΔG.<br /> The model consists of two coupled neural networks, a 3D selfsupervised convolutional neural network that produces a reduceddimensionality representation of the structural environment of a given residue, and a downstream supervised fully-connected neural network that, using the former network's structural representation as input, predicts the ΔΔG of any given amino-acid mutation. The first network is trained on a large dataset of protein structures, and the second network is trained using a dataset of the ΔΔG values of all mutants of 35 proteins, predicted by the biophysics-based method Rosetta.

The paper shows that RaSP gives good approximations of Rosetta ΔΔG predictions while being several orders of magnitude faster. As compared to experimental data, judging by a comparison made for a few proteins, RaSP and Rosetta predictions perform similarly. In addition, it is shown that both RaSP and Rosetta are robust to variations of input structure, so good predictions are obtained using either structures predicted by homology or structures predicted using AlphaFold2.<br /> Finally, the usefulness of a rapid approach such as RaSP is clearly demonstrated by applying it to calculate ΔΔG values for all mutations of a large dataset of human proteins, for which this method is shown to reproduce previous findings of the overall ΔΔG distribution and the relationship between ΔΔG and the pathological consequences of mutations. The RaSP tool and the dataset of mutations of human proteins are shared.

Strengths:

The single main strength of this work is that the model developed, RaSP, is much faster than Rosetta (5 to 6 dex), and still produces ΔΔG predictions of comparable accuracy (as compared with Rosetta, and with the experiment). The usefulness of such a rapid approach is convincingly demonstrated by its application to predicting the ΔΔG of all single-point mutations of a large dataset of human proteins, for which using this new method they reproduce previous findings on the relationship between stability and disease. Such a large-scale calculation would be prohibitive with Rosetta. Importantly, other researchers will be able to take advantage of the method because the code and data are shared, and a google colab site where RaSP can be easily run has been set up. An additional bonus is that the dataset of human proteins and their RaSP ΔΔG predictions, annotated as beneficial/pathological (according to the ClinVar database) and/or by their allele frequency (from the gnomAD database) are also made available, which may be very useful for further studies.

Weaknesses:

The paper presents a solid case in support of the speed, accuracy, and usefulness of RaSP. However, it does suffer from a few weaknesses.

The main weakness is, in my opinion, that it is not clear where RaSP is positioned in the accuracy-vs-speed landscape of current ΔΔGprediction methods. The paper does show that RaSP is much faster than Rosetta, and provides evidence that supports that its accuracy is comparable with that of Rosetta, but RaSP is not compared to any other method. For instance, FoldX has been used in large-scale studies of similar size to the one used here to exemplify RaSP. How does RaSP compare with FoldX? Is it more accurate? Is it faster? Also, as the paper mentions in the introduction, several ML methods have been developed recently; how does RaSP compare with them regarding accuracy and CPU time? How RaSP fares in comparison with other fast approaches such as FoldX and/or ML methods will strongly affect the potential usefulness and impact of the present work.

Second, this work being about presenting a new model, a notable weakness is that the model is not sufficiently described. I had to read a previous paper of 2017 on which this work builds to understand the self-supervised CNN used to model the structure, and even so, I still don't know which of 3 different 3D grids used in that original paper is used in the present work.

A third weakness is, I think, that a stronger case needs to be made for fitting RaSP to Rosetta ΔΔG predictions rather than experimental ΔΔGs. The justification put forward by the authors is that the dataset of Rosetta predictions is large and unbiased while the dataset of experimental data is smaller and biased, which may result in overfitting. While I understand that this may be a problem and that, in general, it is better to have a large unbiased dataset in place of a small biassed one, it is not so obvious to me from reading the paper how much of a problem this is, and whether trying to fix it by fitting the model to the predictions of another model rather than to empirical data does not introduce other issues.

Finally, the method is claimed to be "accurate", but it is not clear to me what this means. Accuracy is quantified by the correlation coefficient between Rosetta and RaSP predictions, R = 0.82, and by the Mean Absolute Error, MAE = 0.73 kcal/mol. Also, both RaSP and Rosetta have R ~ 0.7 with experiment for the few cases where they were tested on experimental data. This seems to be a rather modest accuracy; I wouldn't claim that a method that produces this sort of fit is "accurate". I suppose the case is that this may be as accurate as one can hope it to be, given the limitations of current experimental data, Rosetta, RaSP, and other current methods, but if this is the case, it is not clearly discussed in the paper.

We thank the reviewer for their detailed comments and suggestions.

As discussed in our general comments above and also below, we have now added additional benchmarking, making it easier to compare the accuracy of RaSP with other methods. Regarding the model description, we have now added a more detailed description of also the 3D CNN.

Regarding whether to fit the model to experiments or computational data, we agree that it is not clear cut that the former would also not work. Indeed, a main problem is that in both cases it is hard to answer which approach is better because of the scarcity of experimental data. One major problem with the larger sets of experimental data is, as we mention, the bias and variability; another is the provenance. While some databases exist, they are rarely exactly raw data, and for example may contain ∆∆G values estimated from ∆Tm values. In the revised manuscript we now explain better why we chose to target Rosetta, but also acknowledge that one might also have used experiments.

As to the question of accuracy, we agree completely that the methods could be better. One problem, however, is that it is very difficult to answer how much better because of problems with experiments. As mentioned also by reviewer 1, variation across different experiments suggest that even a “perfect” predictor would only achieve Pearson correlation coefficients in the range 0.7–0.8 (https://doi.org/10.1093/bioinformatics/bty880). Clearly, this is an issue with imperfect data curation (it is possible to measure ∆∆G quite accurately), but in the absence of larger and better curated experiments, one will not expect much better accuracy than what we report here. This is now discussed in the revised manuscript.

Reviewer 3 (Public Review):

The authors present a machine learning method for predicting the effects of mutations on the free energy of protein stability. The method performs similarly to existing methods, but has the advantage that it is faster to run. Overall this is reasonable and a faster method will likely have some potential uses. However, not improving performance beyond the reasonable but not great performance of existing methods of course makes this a less useful advance. The authors provide predictions for a set of human proteins, but the impact of their method would be much greater if they provided predictions for all substitutions in all human proteins, for example. In places the text somewhat overstates the performance of computational methods for predicting free energy changes and is potentially misleading about when ddGs are predicted vs. experimentally measured. In addition, the comparison to existing methods is rather slim and there isn't a formal evaluation of how well RASP discriminates pathological from benign variants.

We thank the reviewer for taking time to read our work and for their various suggestions.

Author Response

Reviewer #1 (Public Review):

Alignment between high dimensional data which express their dynamics in a subspace is a challenge which has recently been addressed both with analytic-based solutions like the Procrustes transformation, and, most interestingly, via deep learning approaches based on adversarial networks. The authors have previously proposed an adversarial network approach for alignment which relied on first dimensionally-reducing the binned neural spikes using an autoencoder. Here, they use an alternative approach to align data without use of an initial dimensional-reduction step.

The results are fairly clear - the Cycle-GAN approach works better than their previous ADAN approach and one based on dimensionality reduction followed by the Procrustes transform. In general, a criticism of this entire field is to understand what alignment teaches us about the brain or how it specifically will be used in a BCI context.

There are a few issues with the paper.

1.) To increase the impact of their work, the investigators have now used it to align data in multiple types of tasks. There was an unanswered question about this related to neuroscience - does alignment in one task predict alignment for another?

This is a great question! We anticipate that it will be challenging for an alignment learned on one task to be used on another task, because we know that M1 decoders trained on data from one behavior often do not generalize when tested using a different behavior (Naufel et al., 2019)*. The same nonlinearities that prevent zero-shot decoding across tasks are also likely to impair the ability of an aligner trained on data from one task to successfully align data from another task. Furthermore, the results of Naufel et al. indicate that even if neural alignment is successful, we would need a decoder already trained on the new task to produce reliable predictions-- in which case the data needed to train that decoder could simply be used for alignment. A systematic study of the relation between the ability to align and decode from data is well warranted, but beyond the scope of our current work.

*Naufel, S., Glaser, J. I., Kording, K. P., Perreault, E. J., & Miller, L. E. (2019). A muscle-activity-dependent gain between motor cortex and EMG. Journal of neurophysiology, 121(1), 61-73.

Action in the text: none.

2) Investigators use decoding as a way of comparing alignment performance. The description of the cycle GAN was not super detailed, and it wasn't clear whether there was any dynamic information stored in the network that might create questions of causality in actual use. It seems that input is simply the neural activity at a current time point rather than neural activity across the trial, which would alleviate this concern. However, they mention temporal alignment but never describe in detail whether all periods of spikes are properly modeled by the system or if only subsets of data (specific portions of task or non-task time) will work. Perhaps this is more a question of the Wiener filter, for which precise details are missing.

As intuited by the reviewer, we did only use the neural activity at a current time point as the inputs for Cycle-GAN training, so the system is causal and can be used in real time. We have modified the text to clarify this.

We apologize for any confusion caused by our use of the term "temporal alignment", which was for the sake of consistency with earlier-published, CCA-based alignment methods (e.g., in Gallego et al., 2020), but is indeed confusing. In the revised manuscript, we have switched to the term ‘trial alignment’ which we believe better reflects this pre-processing step, and we have included additional explanations in the introduction.

Importantly, while CCA-style trial alignment is not required by our methods, we do still preprocess our data to exclude behaviors not related to the investigated task. Since monkeys were resting or performing task-irrelevant movements during inter-trial period, we chose to use data only from trial start to trial end, but without any explicit trial matching or alignment (see Appendix 1 - Behavior tasks). In the revised manuscript, we now show that our methods still works well when applied even to the continuous recordings, with Cycle-GAN significantly outperforming both ADAN and PAF.

Action in the text (page 2, lines 72-74): clarifying CCA description and replacing “temporal alignment” with “trial alignment”.

Action in the text (page 5, lines 191-192): stating that ADAN and Cycle-GAN have no knowledge of dynamics.

Action in the text (page 6, lines 258-272): documenting performance on full-day recordings without trial matching.

Action in the text (page 13, lines 647-649): again, stating that Cycle-GAN has no knowledge of dynamics.

3) In general, precise details of the algorithms should have been provided.

We appreciate the reviewer noting this-- in the submitted manuscript, the full descriptions of Cycle-GAN and ADAN were included as supplementary methods in Appendix 4, but we did not extensively reference this and it may have been missed. In the revised manuscript, we added more references to Appendix 4 and in the Methods section of the main text. We provided further details on the choice of hyperparameters for each method (including PAF) in Appendix 4 itself.

Action in the text (page 13, lines 643-644): added “For a full description of the ADAN architecture and its training strategy, please refer to “ADAN based aligner” in Appendix 4 and (Farshchian et al., 2018).”

Action in the text (page 14, lines 669): added “Further details about the Cycle-GAN based aligner are provided in “Cycle-GAN based aligner”, Appendix 4.” Action in the text (Appendix 4 Tables 1-2): We have added a summary table of hyperparameters for each method in Appendix 4 (ADAN: Appendix 4 Table 1; CycleGAN: Appendix 4 Table 2).

4) Cross validation for day-0 alignment is not explained.

As mentioned above, the training and validation details of day-0 models were included in Appendix 4, which was not extensively referenced in the manuscript and may have been missed. We have now added more references to the Appendix in the revised manuscript.

Action in the text (page 13, lines 627-629): added “(Note that this LSTM based decoder is only used for latent space discovery, not the later decoding stage that is used for performance evaluation (see “ADAN day-0 training” in Appendix 4 for full details)).”

5) Details of statistical tests is not provided.

We apologize for this omission. In the revised manuscript, we have added a section in the methods summarizing all the statistical tests. In addition, we added the sample sizes for each stat reported in the results section.

Action in the text (page 15, lines 754-768): new Methods section added.

6) (minor) The idea that for neurons that have disappeared that the CycleGAN can "infer their response properties", seems an incorrect description. A proper description should be that it "hallucinates" their response properties?

We prefer to avoid the term “hallucinate”, due to its recent increased (appropriate) use in the context of large language models describing content generation that is “nonsensical or unfaithful to the provided source content” (as per the Wikipedia article on hallucination in AI). The synthetized “responses” of vanished neurons are not nonsensical, but are indeed, inferred: they are the model’s best estimate of how these neurons would have responded, had they been observed. While not explored further here, this prediction could be of potential scientific use: a strong discrepancy between predicted and observed activity might be a clue to look for further evidence of learning or remodeling of neural representations of behavior.

Action in the text: none.

Reviewer #2 (Public Review):

In this manuscript, the authors use generative adversarial networks (GANs) to manipulate neural data recorded from intracortical arrays in the context of intracortical BCIs so that these decoders are robust. Specifically, the authors deal with the hard problem where signals from an intracortical array change over time and decoders that are trained on day 0 do not work on day K. Either the decoder or the neural data needs to be updated to achieve the same performance as initially. GANs try to alter the neural data from day K to make it indistinguishable to day 0 and thus in principle the decoder should perform better. The authors compare their GAN approach to an older GAN approach (by an overlapping group of authors) and suggest that this new GAN approach is somewhat better. Major Strengths are multiple datasets from behaving monkeys performing various tasks that involve motor function. Comparison between two different GAN approaches and a classical approach that uses factor analysis. The weakness is insufficient comparison to another state-of-the-art approach that has been applied on the same dataset (NoMAD, Karpowicz et al. BioRxiv.)

The results are very reasonable and they show their approach, Cycle GANs, does slightly better than the traditional GAN approach. However, the Cycle GANs have many more modules and also as I understand it performs a forward backward mapping of the day - 0 and day - k and thus theoretically better. But, it seems quite slow.

We are concerned that the reviewer may have mistaken the Cycle-GAN training time (the time it takes to find an alignment, Figure 4B) with its inference time (the time it takes to transform data once an alignment has been found). Whereas inference time is critical for practical deployment of a model, we argue that Cycle-GAN's somewhat longer training time is not a substantial barrier to use: it is still reasonably fast (a few minutes) and training will only need to be performed on the order of once per day. We have modified the y-axis label of Figure 4B to make this distinction clearer.

We have also now added information on the inference speed of trained models to the paper: we find that both Cycle-GAN and ADAN perform the inference step in under 1 ms per 50 ms sample of data – this is because the forward map in both models consists of a fully connected network with only two hidden layers. We also note that while forward-backward mapping between days does occur during Cycle-GAN training, only the forward mapping is performed during inference.

Action in the text (page 7, lines 303-306): added inference time for Cycle-GAN and ADAN.

I think the results are interesting but as such, I am not sure this is such a fundamental advance compared to the Farashcian et al. paper, which introduced GANs to improve decoding in the face of changing neural data. There are other approaches that also use GANs and I think they all need to be compared against each other. Finally, these are all offline results and what happens online is anyone's real guess. Of course, this is not just a weakness of this study but many such studies of its ilk.

Author Response

Reviewer #1 (Public Review):

The manuscript by Gochman and colleagues reports the discovery of a very strong sensitization of TRPV2 channels by the herbal compound cannabidiol (CBD) to activation by the synthetic agonist 2aminoethoxydiphenyl borate (2-APB). Using patch-clamp electrophysiology the authors show that the ~100-fold enhancement by micromolar CBD of TRPV2 current responses to low concentrations of 2-APB reflects a robust increase in apparent affinity for the latter agonist. Cryo-EM structures of TRPV2 in lipid nanodiscs in the presence of both drugs report two-channel conformations. One conformation resembles previously solved structures whereas the second conformation reveals two distinct CBD binding sites per subunit, as well as changes in the conformation of the S4-S5 linker. Interestingly, although TRPV1 and TRPV3 are highly homologous to TRPV2 and both CBD binding sites are relatively conserved, the CBD-induced sensitization towards 2-APB is observable only for TRPV3 but not for TRPV1. Moreover, the simultaneous substitution of non-conserved residues in the CBD binding sites and the pore region of TRPV1 with the amino acids present in TRPV2 fails to confirm strong CBD-induced sensitization. The authors conclude that CBD-dependent sensitization of TRPV2 channels depends on structural features of the channel that are not restricted to the CBD binding site but involve multiple channel regions.

These are important findings that promote our understanding of the molecular mechanisms of TRPV family channels, and the data provide convincing evidence for the conclusions.

We appreciate the supportive evaluation of the reviewer.

Reviewer #2 (Public Review):

In this manuscript, Gochman et al. studied the molecular mechanism by which cannabidiol (CBD) sensitizes the TRPV2 channel to activation by 2-APB. While CBD itself can activate TRPV2 with low efficacy, it can sensitize TRPV2 current activated by 2-APB by two orders of magnitude. The authors showed, via single-channel recording, that the CBD-dependent sensitization arises from an increase in Po when the channel binds to both CBD and 2-APB. The authors then used cryo-EM to investigate how CBD binds to TRPV2 and identified two CBD binding sites in each subunit, with one site being previously reported and the other being newly discovered.

TRPV1 and TRPV2 are two channels closely related to TRPV2. All three channels can be activated by CBD and 2-APB, but only TRPV2 and 3 are strongly sensitized by CBD. To understand the molecular basis of the different sensitivity to CBD, the authors compared the residues within the CBD binding sites and generated mutants by swapping non-conserved residues between TRPV1 and TRPV2. They then performed patch-clamp recordings on these mutants and found that mutations on non-conserved residues indeed influenced the CBD-dependent sensitization, thereby supporting the observed CBD binding sites.

Unexpectedly, the authors did not identify the binding site of 2-APB, despite its robust effect in electrophysiology recordings, especially when combined with CBD. Although previous structural studies of TRPV2 have reported 2-APB binding sites, the associated densities in these studies were not wellresolved. Therefore, the authors called on the field to re-examine published structural data with regard to the 2-APB binding sites.

Overall, this is an important study with well-designed and well-conducted experiments.

We appreciated the supportive comments of the reviewer.

Reviewer #3 (Public Review):

In this paper, Gochman et al examine TRPV1-3 channel sensitization by CBD, specifically in the context of 2-APB activation. The authors primarily used classic electrophysiological techniques to address their questions about channel behavior but have also used structural biology in the form of cryo-EM to examine drug binding to TRPV2. The authors have carefully observed and quantified sensitization of the rat TRPV2 channel to 2-APB by CBD. While this sensitization has been reported previously (Pumroy et al, Nat Commun 2022), the authors have gone into much more detail here and carefully examined this process from several angles, including a comparison to some other known methods of sensitizing TRPV2. Additionally, the authors have also revealed that CBD sensitizes rat TRPV1 and mouse TRPV3 to 2-APB, which has not been reported previously. Up to this point, the work is well thought through and cohesive.

The major weakness of this paper is that the authors' efforts to track down the structural and molecular basis for CBD sensitization neither give insight into how sensitization occurs nor provide a solid footing for future work on the topic. The structural work presented in this paper lacks proper controls to interpret the observed states and the authors do nothing to follow up on a potentially interesting second binding site for CBD. Overall, the structural work feels detached from the rest of the paper. The mutations chosen to examine sensitization are based on setting up TRPV1 in opposition to TRPV2 and TRPV3, which makes little sense as all three channels show sensitization by CBD, even if to different extents. The authors chose their mutations based on the assumption that response to CBD is the key difference between the channels for sensitization, yet the overall state of each channel or the different modes of activation by 2-APB seem to be more likely candidates. As a result, it is not particularly surprising that none of the mutations the authors make reduce CBD sensitization in TRPV2 or increase CBD sensitization in TRPV1.

A difficulty in examining TRPV1-3 as a group is that while they are highly conserved in sequence and structure, there are key differences in drug responses. While it does seem likely that CBD would bind to the same location in TRPV1-3, there is extensive evidence that 2-APB binds at different sites in each channel, as the authors discuss in the paper. Without more basic information about where 2-APB binds to each channel and confirmation that CBD does indeed bind TRPV1-3 at the same site, it may not be possible to untangle this particular mode of channel sensitization.

We appreciate this reviewer’s perspective and we too were disappointed that our approach did not yield more definitive answers to why some TRPV channels are more sensitive to CBD. We have revised the results and discussion sections to more clearly articulate what we think our results reveal. We have also added a section to the discussion to present the idea that the differential sensitivity of TRPV channels to CBD may have more to do with where 2-APB binds and how it activates the channel than CBD. These challenging points are all excellent and they have helped us to present our message more clearly.

Author Response

Reviewer #1 (Public Review):

The authors introduce a computational model that simulates the dendrites of developing neurons in a 2D plane, subject to constraints inspired by known biological mechanisms such as diffusing trophic factors, trafficked resources, and an activity-dependent pruning rule. The resulting arbors are analyzed in terms of their structure, dynamics, and responses to certain manipulations. The authors conclude that 1) their model recapitulates a stereotyped timecourse of neuronal development: outgrowth, overshoot, and pruning 2) Neurons achieve near-optimal wiring lengths, and Such models can be useful to test proposed biological mechanisms- for example, to ask whether a given set of growth rules can explain a given observed phenomenon - as developmental neuroscientists are working to understand the factors that give rise to the intricate structures and functions of the many cell types of our nervous system.

Overall, my reaction to this work is that this is just one instantiation of many models that the author could have built, given their stated goals. Would other models behave similarly? This question is not well explored, and as a result, claims about interpreting these models and using them to make experimental predictions should be taken warily. I give more detailed and specific comments below.

We thank the reviewer for the summary of the work. We find the criticism “that this is one instantiation of many models [we] could have built” can apply to any model. To quote George Box, “all models are wrong, but some models are useful” was the moto that drove our modeling approach. In principle, there are infinitely many possible models. We chose one of the most minimalistic models which implements known biological mechanisms including activity-independent and -dependent phases of dendritic growth, and constrained parameters based on experimental data. We compare the proposed model to other alternatives in the Discussion section, especially to the models of Hermann Cuntz which propose very different strategies for growth.

However, the reviewer is right that within the type of model we chose, we could have more extensively explored the sensitivity to parameters. In the revised manuscript we will investigate the sensitivity of model output to variations of specific parameters, as explained below.

Point 1.1. Line 109. After reading the rest of the manuscript, I worry about the conclusion voiced here, which implies that the model will extrapolate well to manipulations of all the model components. How were the values of model parameters selected? The text implies that these were selected to be biologically plausible, but many seem far off. The density of potential synapses, for example, seems very low in the simulations compared to the density of axons/boutons in the cortex; what constitutes a potential synapse? The perfect correlations between synapses in the activity groups is flawed, even for synapses belonging to the same presynaptic cell. The density of postsynaptic cells is also orders of magnitude of, etc. Ideally, every claim made about the model's output should be supported by a parameter sensitivity study. The authors performed few explorations of parameter sensitivity and many of the choices made seem ad hoc.

It is indeed important to clarify how the model parameters were selected. Here we provide a short justification for some of these parameters, which will be included in the revised manuscript.

1) Potential synapse density: We modelled 1,500 potential synapses in a cortical sheet of size 185x185 microns squared. We used 1 pixel per μm to capture approximately 1 μm thick dendrites. Therefore, we started with initial density of 0.044 potential synapses per μm^2. From Author Response Image 1 we can see that at the end of our simulation time ~1,000 potential synapses remain. So in fact, the density of potential synapses is totally sufficient, since not many potential synapses end up connected. The rapid slowing down of growth in our model is not due to a depletion of potential synaptic partners as the number of potential synapses remains high. Nonetheless, we will explore this in the revised manuscript. (this figure will be included in the revised submission):

2) Stabilized synapse density: Since ~1,000 of the potential synapses in the modeled cortical sheet remain available, ~500 become connected to the dendrites of the 9 somas in the modeled cortical sheet. This means that the density of stable connected synapses is approximately 0.015 synapses per μm^2. This is also the number that is shown in Figure 3b, which is about 60 synapses stabilized per cell. This density is much easier to compare to experimental data, and below we provide some numbers from literature we already cited in the manuscript as well as a recent preprint.

In the developing cortex:

• Leighton, Cheyne and Lohmann 2023 https://doi.org/10.1101/2023.03.02.530772 find up to 0.4 synapses per μm in pyramidal neurons in vivo in the developing mouse visual cortex at P8 to P13. This is almost identical to our value of 0.4 synapses per μm.

• Ultanir et al., 2007 https://doi.org/10.1073/pnas.0704031104 find 0.7 to 1.7 spines per μm in pyramidal neurons in vivo in L2/3 of the developing mouse cortex, at P10 to P20.

• Glynn et al., 2011 https://doi.org/10.1038/nn.2764 find 0.1 to 0.7 spines per μm^2 in pyramidal neurons in vivo and in vitro in L2/3 of the developing mouse cortex, at P8 to P60.

In the developing hippocampus:

• Yang et al., 2014 https://doi.org/10.1016/j.celrep.2014.03.040 find 0.75 to 1 spines per μm in pyramidal neurons in vivo in CA1 of the developing mouse hippocampus, at one month of age.

• Koshimizu et al., 2009 https://doi.org/10.1186/1756-6606-2-27 find 0.1 to 0.4 spines per μm in pyramidal neurons in slice in the developing rat hippocampus, at (Embryonic Day) ED18 to ED20.

• Tyler and Pozzo-Miller, 2001 https://doi.org/10.1523/JNEUROSCI.21-12-04249.2001 find 0.28 to 0.1 spines per μm in slice in the developing mouse hippocampus, at P7 (14 DIV, days in vitro).

Although these values vary somewhat across experiments, in most cases they are in agreement with our chosen values, especially when taking into account that we are modeling development (rather than adulthood).

3) Soma/neuron density: Indeed, we did not exactly mention this number anywhere in the paper. But from the figures we can infer 9 somas growing dendrites on an area of ~34,000 μm^2. Thus, neuron density would be 300 neurons per mm^2. This number seems a bit low after a short search through the literature. For e.g. Keller et al., 2018 https://www.frontiersin.org/articles/10.3389/fnana.2018.00083/full reports about 90,000 neurons per mm^3, albeit in adulthood.

We are also performing a sensitivity analysis where some of these parameters are varied and will include this in the revised manuscript. In particular:

(1) We will vary the nature of the input correlations. In the current model, the synapses in each correlated group receive spike trains with a perfect correlation and there are no correlations across the groups. We will reduce the correlations within group and add non-zero correlations across the groups.

(2) We will vary the density of the neuronal somas. We expect that higher densities of somas will either yield smaller dendritic areas because the different neurons compete more or result in a state where nearby neurons have to complement each other regarding their activity preferences.

(3) We will introduce dynamics in the potential synapses to model the dynamics of axons. We plan to explore several scenarios. We could introduce a gradual increase in the density of potential synapses and implement a cap on the number of synapses that can be alive at the same time, and vary that cap. We could also introduce a lifetime of each synapse (following for example a lognormal distribution). A potential synapse can disappear if it does not form a stable synapse in its lifetime, in which case it could move to a different location.

Point 1.2. Many potentially important phenomena seem to be excluded. I realize that no model can be complete, but the choice of which phenomena to include or exclude from this model could bias studies that make use of it and is worth serious discussion. The development of axons is concurrent with dendrite outgrowth, is highly dynamic, and perhaps better understood mechanistically. In this model, the inputs are essentially static. Growing dendrites acquire and lose growth cones that are associated with rapid extension, but these do not seem to be modeled. Postsynaptic firing does not appear to be modeled, which may be critical to activity-dependent plasticity. For example, changes in firing are a potential explanation for the global changes in dendritic pruning that occur following the outgrowth phase.

As the reviewer concludes, no model can be complete. In agreement with this, here we would like to quote a paragraph from a very nice paper by Larry Abbott (“Theoretical Neuroscience Rising, Neuron 2008 https://www.sciencedirect.com/science/article/pii/S0896627308008921) which although published more than 10 years ago, still applies today:

“Identifying the minimum set of features needed to account for a particular phenomenon and describing these accurately enough to do the job is a key component of model building. Anything more than this minimum set makes the model harder to understand and more difficult to evaluate. The term ‘‘realistic’’ model is a sociological rather than a scientific term. The truly realistic model is as impossible and useless a concept as Borges’ ‘‘map of the empire that was of the same scale as the empire and that coincided with it point for point’’ (Borges, 1975). […] The art of modeling lies in deciding what this subset should be and how it should be described.”

We have clearly stated in the Introduction (e.g. lines 37-75) which phenomena we include in the model and why. The Discussion also compares our model to others (lines 315-373), pointing out that most models either focus on activity-independent or activity-dependent phases. We include both, combining literature on molecular gradients and growth factors, with activity-dependent connectivity refinements instructed by spontaneous activity. We could not think of a more tractable, more minimalist model that would include both activity-independent or activity-dependent aspects. Therefore, we feel that the current manuscript provides sufficient motivation but also a discussion of limitations of the current model.

Regarding including the concurrent development of axons, we agree this is very interesting and currently not addressed in the model. As noted at the bottom of our reply to point 1.1, bullet (3) we are now revising the manuscript to include a simplified form of axonal dynamics by allowing changes in the lifetime and location of potential synapses, which come from axons of presynaptic partners.

Regarding postsynaptic firing, this is indeed super relevant and an important point to consider. In one of our recent publications (Kirchner and Gjorgjieva, 2021 https://www.nature.com/articles/s41467-021-23557-3), we studied only an activity-dependent model for the organization of synaptic inputs on non-growing dendrites which have a fixed length. There, we considered the effect of postsynaptic firing and demonstrated that it plays an important role in establishing a global organization of synapses on the entire dendritic tree of the neuron, and not just local dendritic branches. For example, we showed that could that it could lead to the emergence of retinotopic maps which have been found experimentally (Iacaruso et al., 2017 https://www.nature.com/articles/nature23019). Since we use the same activity-dependent plasticity model in this paper, we expect that the somatic firing will have the same effect on establishing synaptic distributions on the entire dendritic tree. We will make a note of this in the Discussion in the revised paper.

Point 1.3. Line 167. There are many ways to include activity -independent and -dependent components into a model and not every such model shows stability. A key feature seems to be that larger arbors result in reduced growth and/or increased retraction, but this could be achieved in many ways (whether activity dependent or not). It's not clear that this result is due to the combination of activity-dependent and independent components in the model, or conceptually why that should be the case.

We never argued for model uniqueness. There are always going to be many different models (at different spatial and temporal scales, at different levels of abstraction). We can never study all of them and like any modeling study in systems neuroscience we have chosen one model approach and investigated this approach. We do compare the current model to others in the Discussion. If the reviewers have a specific implementation that we should compare our model to as an alternative, we could try, but not if this means doing a completely separate project.

Point 1.4. Line 183. The explanation of overshoot in terms of the different timescales of synaptic additions versus activity-dependent retractions was not something I had previously encountered and is an interesting proposal. Have these timescales been measured experimentally? To what extent is this a result of fine-tuning of simulation parameters?

We found that varying the amount of BDNF controls the timescale of the activity-dependent plasticity (see our Figure 5c). Hence, changing the balance between synaptic additions vs. retractions is already explored in Figure 5e and f. Here we show that the overshoot and retraction does not have to be fine-tuned but may be abolished if there is too much activity-dependent plasticity.

Regarding the relative timescales of synaptic additions vs. retractions: since the first is mainly due to activity-independent factors, and the second due to activity-dependent plasticity, the questions is really about the timescales of the latter two. As we write in the Introduction (lines 60-62), manipulating activity-dependent synaptic transmission has been found to not affect morphology but rather the density and specificity of synaptic connections (Ultanir et al. 2007 https://doi.org/10.1073/pnas.0704031104), supporting the sequential model we have (although we do not impose the sequence, as both activity-independent and activity-dependent mechanisms are always “on”; but note that activity-dependent plasticity can only operate on synapses that have already formed).

Point 1.5. Line 203. This result seems at odds with results that show only a very weak bias in the tuning distribution of inputs to strongly tuned cortical neurons (e.g. work by Arthur Konnerth's group). This discrepancy should be discussed.

First, we note that the correlated activity experienced by our modeled synapses (and resulting synaptic organization) does not necessarily correspond to visual orientation, or any stimulus feature, for that matter.

Nonetheless, this is a very interesting question and there is some variability in what the experimental data show. Many studies have shown that synapses on dendrites are organized into functional synaptic clusters: across brain regions, developmental ages and diverse species from rodent to primate (Kleindienst et al. 2011; Takahashi et al. 2012; Winnubst et al. 2015; Gökçe et al., 2016; Wilson et al. 2016; Iacaruso et al., 2017; Scholl et al., 2017; Niculescu et al. 2018; Kerlin et al. 2019; Ju et al. 2020). Interestingly, some in vivo studies have reported lack of fine-scale synaptic organization (Varga et al. 2011; X. Chen et al. 2011; T.-W. Chen et al. 2013; Jia et al. 2010; Jia et al. 2014), while others reported clustering for different stimulus features in different species. For example, dendritic branches in the ferret visual cortex exhibit local clustering of orientation selectivity but do not exhibit global organization of inputs according to spatial location and receptive field properties (Wilson et al. 2016; Scholl et al., 2017). In contrast, synaptic inputs in mouse visual cortex do not cluster locally by orientation, but only by receptive field overlap, and exhibit a global retinotopic organization along the proximal-distal axis (Iacaruso et al., 2017). We proposed a theoretical framework to reconcile these data: combining activity-dependent plasticity similar to the BDNF-proBDNF model that we used in the current work, and a receptive field model for the different species (Kirchner and Gjorgjieva, 2021 https://www.nature.com/articles/s41467-021-23557-3). We can mention this aspect in the revised manuscript.

Point 1.6. Line 268. How does the large variability in the size of the simulated arbors relate to the relatively consistent size of arbors of cortical cells of a given cell type? This variability suggests to me that these simulations could be sensitive to small changes in parameters (e.g. to the density or layout of presynapses).

As noted at the bottom of our reply to point 1.1, bullet (3) we are now revising the manuscript to include changes in the lifetime and location of potential synapses.

Point 1.7. The modeling of dendrites as two-dimensional will likely limit the usefulness of this model. Many phenomena- such as diffusion, random walks, topological properties, etc - fundamentally differ between two and three dimensions.

The reviewer is right about there being differences between two and three dimensions. But a simpler model does not mean a useless model even if not completely realistic. We have ongoing work that extends the current model to 3D but is beyond the scope of the current paper. In systems neuroscience, people have found very interesting results making such simplified geometric assumptions about networks, for instance the one-dimensional ring model has been used to uncover fundamental insights about computations even though highly simplified and abstracted.

Point 1.8. The description of wiring lengths as 'approximately optimal' in this text is problematic. The plotted data show that the wiring lengths are several deviations away from optimal, and the random model is not a valid instantiation of the 2D non-overlapping constraints the authors imposed. A more appropriate null should be considered.

We did not use the term “optimal” in line with previous literature. We wrongly referred to the minimal wiring length as the optimal wiring length, but neurons can optimize their wiring not only by minimizing their dendritic length (e.g. work of Hermann Cuntz). In the revised manuscript, we will replace the term “optimal wiring” with “minimal wiring”. Then we will compare the wiring length in the model with the theoretically minimal wiring length, the random wiring length and the actual data.

Point 1.9. It's not clear to me what the authors are trying to convey by repeatedly labeling this model as 'mechanistic'. The mechanisms implemented in the model are inspired by biological phenomena, but the implementations have little resemblance to the underlying biophysical mechanisms. Overall my impression is that this is a phenomenological model intended to show under what conditions particular patterns are possible. Line 363, describing another model as computational but not mechanistic, was especially unclear to me in this context.

What we mean by mechanistic is that we implement equations that model specific mechanisms i.e. we have a set of equations that implement the activity-independent attraction to potential synapses (with parameters such as the density of synapses, their spatial influence, etc) and the activity-dependent refinement of synapses (with parameters such as the ratio of BDNF and proBDNF to induce potentiation vs depression, the activity-dependent conversion of one factor to the other, etc). This is a bottom-up approach where we combine multiple elements together to get to neuronal growth and synaptic organization. This approach is in stark contrast to the so-called top-down or normative approaches where the method would involve defining an objective function (e.g. minimal dendritic length) which depends on a set of parameters and then applying a gradient descent or other mathematical optimization technique to get at the parameters that optimize the objective function. This latter approach we would not call mechanistic because it involves an abstract objective function (who could say what a neuron or a circuit should be trying to optimize) and a mathematical technique for how to optimize the function (we don’t know of neurons can compute gradients of abstract objective functions).

Hence our model is mechanistic, but it does operate at a particular level of abstraction/simplification. We don’t model individual ion channels, or biophysics of synaptic plasticity (opening and closing of NMDA channels, accumulation of proteins at synapses, protein synthesis). We do, however, provide a biophysical implementation of the plasticity mechanism though the BDNF/proBDNF model which is more than most models of plasticity achieve, because they typically model a phenomenological STDP or Hebbian rule that just uses activity patterns to potential or depress synaptic weights, disregarding how it could be implemented.

Reviewer #2 (Public Review):

This work combines a model of two-dimensional dendritic growth with attraction and stabilisation by synaptic activity. The authors find that constraining growth models with competition for synaptic inputs produces artificial dendrites that match some key features of real neurons both over development and in terms of final structure. In particular, incorporating distance-dependent competition between synapses of the same dendrite naturally produces distinct phases of dendritic growth (overshoot, pruning, and stabilisation) that are observed biologically and leads to local synaptic organisation with functional relevance. The approach is elegant and well-explained, but makes some significant modelling assumptions that might impact the biological relevance of the results.

Strengths:

The main strength of the work is the general concept of combining morphological models of growth with synaptic plasticity and stabilisation. This is an interesting way to bridge two distinct areas of neuroscience in a manner that leads to findings that could be significant for both. The modelling of both dendritic growth and distance-dependent synaptic competition is carefully done, constrained by reasonable biological mechanisms, and well-described in the text. The paper also links its findings, for example in terms of phases of dendritic growth or final morphological structure, to known data well.

Weaknesses:

The major weaknesses of the paper are the simplifying modelling assumptions that are likely to have an impact on the results. These assumptions are not discussed in enough detail in the current version of the paper.

1) Axonal dynamics.

A major, and lightly acknowledged, assumption of this paper is that potential synapses, which must come from axons, are fixed in space. This is not realistic for many neural systems, as multiple undifferentiated neurites typically grow from the soma before an axon is specified (Polleux & Snider, 2010). Further, axons are also dynamic structures in early development and, at least in some systems, undergo activity-dependent morphological changes too (O'Leary, 1987; Hall 2000). This paper does not consider the implications of joint pre- and post-synaptic growth and stabilisation.

We thank the reviewer for the summary of the strengths and weaknesses of the work. While we feel that including a full model of axonal dynamics is beyond the scope of the current manuscript, some aspects of axonal dynamics can be included. In a revised model, we will introduce a gradual increase in the density of potential synapses and implement a cap on the number of synapses that can be alive at the same time, and vary that cap. We plan to also introduce a lifetime of each synapse (following for example a lognormal distribution). A potential synapse can disappear if it does not form a stable synapse in its lifetime, in which case it could move to a different location. See also our reply to reviewer comment 1.1, bullet (3).

2) Activity correlations

On a related note, the synapses in the manuscript display correlated activity, but there is no relationship between the distance between synapses and their correlation. In reality, nearby synapses are far more likely to share the same axon and so display correlated activity. If the input activity is spatially correlated and synaptic plasticity displays distance-dependent competition in the dendrites, there is likely to be a non-trivial interaction between these two features with a major impact on the organisation of synaptic contacts onto each neuron.

We are exploring the amount of correlation (between and within correlated groups) to include in the revised manuscript (see also our reply to reviewer comment 1.1, bullet (1)).

However, previous experimental work, (Kleindienst et al., 2011 https://doi.org/10.1016/j.neuron.2011.10.015) has provided anatomical and functional analyses that it is unlikely that the functional synaptic clustering on dendritic branches is the result of individual axons making more than one synapse (see pg. 1019).

3) BDNF dynamics

The models are quite sensitive to the ratio of BDNF to proBDNF (eg Figure 5c). This ratio is also activity-dependent as synaptic activation converts proBDNF into BDNF. The models assume a fixed ratio that is not affected by synaptic activity. There should at least be more justification for this assumption, as there is likely to be a positive feedback relationship between levels of BDNF and synaptic activation.

The reviewer is correct. We used the BDNF-proBDNF model for synaptic plasticity based on our previous work: Kirchner and Gjorgjieva, 2021 https://www.nature.com/articles/s41467-021-23557-3.

There, we explored only the emergence of functionally clustered synapses on static dendrites which do not grow. In the Methods section (Parameters and data fitting) we justify the choice of the ratio of BDNF to proBDNF from published experimental work. We also performed sensitivity analysis (Supplementary Fig. 1) and perturbation simulations (Supplementary Fig. 3), which showed that the ratio is crucial in regulating the overall amount of potentiation and depression of synaptic efficacy, and therefore has a strong impact on the emergence and maintenance of synaptic organization. Since we already performed all this analysis, we do not expect there will be any differences in the current model which includes dendritic growth, as the activity-dependent mechanism has such a different timescale.

A further weakness is in the discussion of how the final morphologies conform to principles of optimal wiring, which is quite imprecise. 'Optimal wiring' in the sense of dendrites and axons (Cajal, 1895; Chklovskii, 2004; Cuntz et al, 2007, Budd et al, 2010) is not usually synonymous with 'shortest wiring' as implied here. Instead, there is assumed to be a balance between minimising total dendritic length and minimising the tree distance (ie Figure 4c here) between synapses and the site of input integration, typically the soma. The level of this balance gives the deviation from the theoretical minimum length as direct paths to synapses typically require longer dendrites. In the model this is generated by the guidance of dendritic growth directly towards the synaptic targets. The interpretation of the deviation in this results section discussing optimal wiring, with hampered diffusion of signalling molecules, does not seem to be correct.

We agree with this comment. We had wrongly used the term “optimal wiring” as neurons can optimize their wiring not only by minimizing their dendritic length but other factors as noted by the reviewer. In the revised manuscript will replace the term “optimal wiring” with “minimal wiring” and discuss these differences to previous work.

Reviewer #3 (Public Review):

The authors propose a mechanistic model of how the interplay between activity-independent growth and an activity-dependent synaptic strengthening/weaken model influences the dendrite shape, complexity and distribution of synapses. The authors focus on a model for stellate cells, which have multiple dendrites emerging from a soma. The activity independent component is provided by a random pool of presynaptic sites that represent potential synapses and that release a diffusible signal that promotes dendritic growth. Then a spontaneous activity pattern with some correlation structure is imposed at those presynaptic sites. The strength of these synapses follow a learning rule previously proposed by the lab: synapses strengthen when there is correlated firing across multiple sites, and synapses weaken if there is uncorrelated firing with the relative strength of these processes controlled by available levels of BDNF/proBDNF. Once a synapse is weakened below a threshold, the dendrite branch at that site retracts and loses its sensitivity to the growth signal

The authors run the simulation and map out how dendrites and synapses evolve and stabilize. They show that dendritic trees growing rapidly and then stabilize by balancing growth and retraction (Figure 2). They also that there is an initial bout of synaptogenesis followed by loss of synapses, reflecting the longer amount of time it takes to weaken a synapse (Figure 3). They analyze how this evolution of dendrites and synapses depends on the correlated firing of synapses (i.e. defined as being in the same "activity group"). They show that in the stabilized phase, synapses that remain connected to a given dendritic branch are likely to be from same activity group (Figure 4). The authors systemically alter the learning rule by changing the available concentration of BDNF, which alters the relative amount of synaptic strengthening, which in turn affects stabilization, density of synapses and interestingly how selective for an activity group one dendrite is (Figure 5). In addition the authors look at how altering the activity-independent factors influences outgrowth (Figure 6). Finally, one of the interesting outcomes is that the resulting dendritic trees represent "optimal wiring" solutions in the sense that dendrites use the shortest distance given the distribution of synapses. They compare this distribute to one published data to see how the model compared to what has been observed experimentally.

There are many strengths to this study. The consequence of adding the activity-dependent contribution to models of synapto- and dendritogenesis is novel. There is some exploration of parameters space with the motivation of keeping the parameters as well as the generated outcomes close to anatomical data of real dendrites. The paper is also scholarly in its comparison of this approach to previous generative models. This work represented an important advance to our understanding of how learning rules can contribute to dendrite morphogenesis

We thank the reviewer for the positive evaluation of the work and the suggestions below.

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

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Reply to the reviewers

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

The current study uses 3D organotypic rafts to culture primary keratinocytes from Foreskin, Tonsil and Cervix. Further the authors looked at the transcriptomic profiles of each tissue types to study similarities and differences depending on the tissue of origin as well as show the similarity in the tissue specific gene signatures and the ex-vivo samples (data from GTEx). As mentioned by authors Skin and Cervix keratinocytes have been previously cultured on collagen rafts however extending it to Tonsil provides resource and possibility of growing more tissue specific epithelial cells in 3D.

Major comments 1. As the papers focus is to culture epithelial/ epidermal cells on 3D rafts, methods section needs more details about the raft composition, preparation, fibroblast embedding what was the plate size used for raft preparation and culturing of cells on those rafts. What culture media was used for epithelial raft cultures?

We have a detailed published protocol that highlight these details. However, we will expand on some of these details in the manuscript

Results: Figure 1, authors show IF staining's for COL17A1 as marker for basal cells and cornulin for differentiated layers. However, it is important to show how many cells in the basal layer are proliferative? (or how many layers of proliferative cells are present in different epithelia analysed here?) after 14 days majority of cells might already start losing their stemness potential (maybe staining for at least ki67 if staining for basal stem cell marker not possible? Along with loricrin or Involucrin might be good idea).

We will stain for ki67 as suggested. However, based on published data using these raft cultures, we do not expect that many cells will be positive.

This is also important as from supp fig 3 you can see F1 has higher expression of Loricrin, filaggrin etc as compared to all other samples indicating higher diff in this sample. Also, if authors can comment on what was the passage of cells used? And have they observed any difference in the re-epithelization in early passage versus late passage of keratinocytes?

We will expand on this is the updated manuscript. Importantly, we grow these cells in a rho-kinase inhibitor that ‘conditionally’ immortalizes these cells as described (DOI: 10.1172/JCI42297).

It is interesting to see Tonsillar 3D epithelia recapitulate the crypt and surface epithelia and authors also show this with gene expression profile, if possible (Optional), can authors show staining for crypt specific and surface specific markers.

We agree that this is an important control. This will be included.

For all the Supplementary tables where only Ensembl ids are represented, please add gene Id column alongside (it is easier to get biological context from gene id for the reader rather than looking up Ensembl ids). Rename the file names to include the Supplementary file 1, 2, 3?

Since there is 1-to-1 conversion for Ensembl to Gene Id, we elected to not include these. The online app does try tp accommodate this as much as possible. We propose to include two versions of each table. 1 with Ensemble ids only and one with both IDs.

Its excellent to see that in vitro tissue signature matched the in vivo tissue samples (Figure 8) but it will be interesting to show the gene expression differences if found any between the in vitro and in vivo samples that will give insight on the changes as result of in vitro system.

Since the in vivo data will be a mixture of epithelial cells and stroma, these comparisons are not straightforward. However, we are currently examining the use of existing scRNA-Seq data to begin addressing these concerns. This data will be included in the next revision.

Minor comments

1. Abstract: Give sample number (n?) and brief results about the genes that had tissue specific expression pattens.
2. Gene names needs to be in Italics throughout.
3. Introduction: page 5 line 9, authors claim that they based on comparisons they can "identify potential therapeutic targets for various disease" I think this statement either needs experimental evidence or statement / claim needs to be modified.
4. Data submission to GEO???
5. Typo (page 15, line 16 should be "HFK-down", same on page 23 "ectocervix", "endocervix", "uterus", so on, please correct, comma needs to be placed after "
6. Page 24 last line is the heatmap referred here Fig 9B?
7. Fig. 1 legends please indicate what F1, F2, F3, C1--- T1--- represent. Fig 1C Please add axis range/ values for protein atlas data as well.
8. Can authors comment in discussion how was current 3D cervix cells on raft method different from Meyers, C., 1996 3D system?

All these ‘minor’ comments will be addressed.

Reviewer #1 (Significance (Required)):

This article does extend and validate the 3D raft culture method to different epithelial tissues in addition to Skin and cervix. This will be useful for the researchers using co culture systems and interested in understanding epithelial cell and immune cell interactions or host pathogen interacts etc

Describe your expertise: establishing and maintaining primary skin and oral keratinocyte cultures on feeders and 3D cultures on DEDs, Organoid cultures from oral keratinocytes, Oral cancer biology, Histopathology, transcriptomics study, Immuno-oncology.

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

Summary Jackson et al.'s manuscript describes an experiment that directly compares 3D organotypic assays created with primary human epithelial cells from foreskin, cervix and tonsil using histological and bulk RNA sequencing approaches. The authors convincingly show the retention of site-specific histological and transcriptomic differences between the stratified epithelial tissues in culture. Differentially expressed genes are identified and pathway analyses suggest genes that might be involved in the different differentiation processes between these tissue sites and differential regulation of ECM and immune pathways. Differentially expressed genes are used to develop a classifier for tissue identification, which is tested using GTEx data.

Major Comments • The interferon stimulated genes of B cells and macrophages (from Mostafavi et al., 2016) are likely to be very different from those in epithelial cells, so the analysis presented in Figure 9 seems like a stretch to me.

We will include caveats to this interpretation. We are planning stimulation experiments of each tissue to compare IFN responses. However, depending on the outcomes, these may end up being outside of the scope of the current manuscript.

• OPTIONAL: Further data comparing the nature and magnitude of the interferon responses of the three epithelia would improve interest in the manuscript but are not necessary for publication of the current dataset.

See above

Minor Comments • Details of n numbers and what each point represents should be added to Figure 1C. Are these points measurements from 25 um intervals of just one raft per donor? What are 'fields of view' here? Are measurements from one section or from multiple sections per raft? • Page 12 - provide a figure/panel citation for the "micrograph derived from a tonsillectomy" that is suggested for comparison. • In Figure 1 - Figure Supplement 1, how representative of the whole raft are these images? Does the extent of stratification change near to the edge of the collagen gel, for example? How well matched for location within a raft are the images shown? • Page 24 - clarify uses of the phrase "down-regulated in tonsils". Presumably this section refers to tonsil epithelium in 3D organotypic rafts.

Typos • Page 3 - "the cervix is lined with stratified squamous epithelia", should be epithelium. • "J.G. Rheinwald" in in text references. • Page 6 - 'or' not 'and' in first sentence of primary cell culture section.

All these ‘minor’ comments and typos will be addressed.

Reviewer #2 (Significance (Required)):

This highly descriptive study provides a detailed analysis of a bulk RNA sequencing experiment comparing foreskin, cervix and tonsil 3D organotypic rafts. Retained histological and transcriptional differences between epithelial tissues of different origins in organotypic assays are well documented in the literature (e.g., parmoplantar vs non-parmoplantar skin, PMID: 36732947; airway tract, PMID: 32526206) so the observed differences between these three very distinct anatomical tissues are unsurprising overall. The data have been made available via SRA and a shiny web app and are likely to be of interest and use to other researchers working on these tissues in culture. The experiment was performed in matched cell culture conditions so replicates are well-controlled, if limited in number (n=3).

We appreciate this feedback. We agree this is a descriptive study. Nonetheless, we believe there is value in formally demonstrating differences and similarities between these tissues. The provided references will be included to expand our discussion.

I am an epithelial cell biologist specializing in human cell culture models. I do not have sufficient computational background to comment in detail on the RNA sequencing methods or analysis within the manuscript.

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

This is very carefully analysed and written study describing the transcriptional differences between in vitro models of epithelia derived from cervix, foreskin and tonsil tissues. Importantly, they compare the findings to in vivo samples using publicly available data. The findings are significant and will be of interest to the scientific community. I cannot fault the analysis pathways or the conclusions, and the manuscript is a pleasure to read. I recommend it is accepted for publication as is.

Reviewer #3 (Significance (Required)):

This is an important study that is highly significant for researchers interested in epithelia tissue and infection. The data are clearly presented and the analysis is thorough. The authors state that they will make the data publicly available. This will be an important resource for the community.

We appreciate the kind words

Author Response

Reviewer #1 (Public Review):

The authors present a study of visuo-motor coupling primarily using wide-field calcium imaging to measure activity across the dorsal visual cortex. They used different mouse lines or systemically injected viral vectors to allow imaging of calcium activity from specific cell-types with a particular focus on a mouse-line that expresses GCaMP in layer 5 IT (intratelencephalic) neurons. They examined the question of how the neural response to predictable visual input, as a consequence of self-motion, differed from responses to unpredictable input. They identify layer 5 IT cells as having a different response pattern to other cell-types/layers in that they show differences in their response to closed-loop (i.e. predictable) vs open-loop (i.e. unpredictable) stimulation whereas other cell-types showed similar activity patterns between these two conditions. They analyze the latencies of responses to visuomotor prediction errors obtained by briefly pausing the display while the mouse is running, causing a negative prediction error, or by presenting an unpredicted visual input causing a positive prediction error. They suggest that neural responses related to these prediction errors originate in V1, however, I would caution against over-interpretation of this finding as judging the latency of slow calcium responses in wide-field signals is very challenging and this result was not statistically compared between areas.

Surprisingly, they find that presentation of a visual grating actually decreases the responses of L5 IT cells in V1. They interpret their results within a predictive coding framework that the last author has previously proposed. The response pattern of the L5 IT cells leads them to propose that these cells may act as 'internal representation' neurons that carry a representation of the brain's model of its environment. Though this is rather speculative. They subsequently examine the responses of these cells to anti-psychotic drugs (e.g. clozapine) with the reasoning that a leading theory of schizophrenia is a disturbance of the brain's internal model and/or a failure to correctly predict the sensory consequences of self-movement. They find that anti-psychotic drugs strongly enhance responses of L5 IT cells to locomotion while having little effect on other cell-types. Finally, they suggest that anti-psychotics reduce long-range correlations between (predominantly) L5 cells and reduce the propagation of prediction errors to higher visual areas and suggest this may be a mechanism by which these drugs reduce hallucinations/psychosis.

This is a large study containing a screening of many mouse-lines/expression profiles using wide-field calcium imaging. Wide-field imaging has its caveats, including a broad point-spread function of the signal and susceptibility to hemodynamic artifacts, which can make interpretation of results difficult. The authors acknowledge these problems and directly address the hemodynamic occlusion problem. It was reassuring to see supplementary 2-photon imaging of soma to complement this data-set, even though this is rather briefly described in the paper.

We will expand on the discussion of caveats as suggested.

Overall the paper's strengths are its identification of a very different response profile in the L5 IT cells compared other layers/cell-types which suggests an important role for these cells in handling integration of self-motion generated sensory predictions with sensory input. The interpretation of the responses to anti-psychotic drugs is more speculative but the result appears robust and provides an interesting basis for further studies of this effect with more specific recording techniques and possibly behavioral measures.

Reviewer #2 (Public Review):

Summary:

This work investigates the effects of various antipsychotic drugs on cortical responses during visuomotor integration. Using wide-field calcium imaging in a virtual reality setup, the researchers compare neuronal responses to self-generated movement during locomotion-congruent (closed loop) or locomotion-incongruent (open loop) visual stimulation. Moreover, they probe responses to unexpected visual events (halt of visual flow, sudden-onset drifting grating). The researchers find that, in contrast to a variety of excitatory and inhibitory cell types, genetically defined layer 5 excitatory neurons distinguish between the closed and the open loop condition and exhibit activity patterns in visual cortex in response to unexpected events, consistent with unsigned prediction error coding. Motivated by the idea that prediction error coding is aberrant in psychosis, the authors then inject the antipsychotic drug clozapine, and observe that this intervention specifically affects closed loop responses of layer 5 excitatory neurons, blunting the distinction between the open and closed loop conditions. Clozapine also leads to a decrease in long-range correlations between L5 activity in different brain regions, and similar effects are observed for two other antipsychotics, aripripazole and haloperidol, but not for the stimulant amphetamine. The authors suggest that altered prediction error coding in layer 5 excitatory neurons due to reduced long-range correlations in L5 neurons might be a major effect of antipsychotic drugs and speculate that this might serve as a new biomarker for drug development.

Strengths:

• Relevant and interesting research question:

The distinction between expected and unexpected stimuli is blunted in psychosis but the neural mechanisms remain unclear. Therefore, it is critical to understand whether and how antipsychotic drugs used to treat psychosis affect cortical responses to expected and unexpected stimuli. This study provides important insights into this question by identifying a specific cortical cell type and long-range interactions as potential targets. The authors identify layer 5 excitatory neurons as a site where functional effects of antipsychotic drugs manifest. This is particularly interesting as these deep layer neurons have been proposed to play a crucial role in computing the integration of predictions, which is thought to be disrupted in psychosis. This work therefore has the potential to guide future investigations on psychosis and predictive coding towards these layer 5 neurons, and ultimately improve our understanding of the neural basis of psychotic symptoms.

• Broad investigation of different cell types and cortical regions:

One of the major strengths of this study is quasi-systematic approach towards cell types and cortical regions. By analysing a wide range of genetically defined excitatory and inhibitory cell types, the authors were able to identify layer 5 excitatory neurons as exhibiting the strongest responses to unexpected vs. expected stimuli and being the most affected by antipsychotic drugs. Hence, this quasi-systematic approach provides valuable insights into the functional effects of antipsychotic drugs on the brain, and can guide future investigations towards the mechanisms by which these medications affect cortical neurons.

• Bridging theory with experiments

Another strength of this study is its theoretical framework, which is grounded in the predictive coding theory. The authors use this theory as a guiding principle to motivate their experimental approach connecting visual responses in different layers with psychosis and antipsychotic drugs. This integration of theory and experimentation is a powerful approach to tie together the various findings the authors present and to contribute to the development of a coherent model of how the brain processes visual information both in health and in disease.

Weaknesses:

• Unclear relevance for psychosis research

From the study, it remains unclear whether the findings might indeed be able to normalise altered predictive coding in psychosis. Psychosis is characterised by a blunted distinction between predicted and unpredicted stimuli. The results of this study indicate that antipsychotic drugs further blunt the distinction between predicted and unpredicted stimuli, which would suggest that antipsychotic drugs would deteriorate rather than ameliorate the predictive coding deficit found in psychosis. However, these findings were based on observations in wild-type mice at baseline. Given that antipsychotics are thought to have little effects in health but potent antipsychotic effects in psychosis, it seems possible that the presented results might be different in a condition modelling a psychotic state, for example after a dopamine-agonistic or a NMDA-antagonistic challenge. Therefore, future work in models of psychotic states is needed to further investigate the translational relevance of these findings.

We fully agree that it is unclear how the effects of antipsychotics in mice relate to the drug effects that would be observed in schizophrenic patients. It is also correct that the reduction of the difference between closed and open loop locomotion onset response in L5 IT neurons (Figure 4) is not what we would have expected to find under the assumption that psychosis is characterized by a blunted distinction between predicted and unpredicted stimuli. We are not sure how to interpret this finding. However, it is probably important to note that the difference is only reduced when using a normalized comparison. Looking just at the subtraction of the two curves, the difference between closed and open loop locomotion onset responses remains unchanged before and after antipsychotic drug injection. The finding of a decorrelation of layer 5 activity, however, is easier to interpret under the assumption that layer 5 functions as an internal representation. If speech hallucinations, for example, are the consequence of a spurious activation of internal representations in speech processing areas of cortex, then antipsychotics might reduce the probability of these spurious activation events by reducing the lateral influence between layer 5 neurons in different cortical areas.

We do indeed plan to address the question of how antipsychotics influence cortical processing in mouse models of schizophrenia in the future.

• Incomplete testing of predictive coding interpretation

While the investigation of neuronal responses to different visual flow stimuli Is interesting, it remains open whether these responses indeed reflect internal representations in the framework of predictive coding. While the responses are consistent with internal representation as defined by the researchers, i.e., unsigned prediction error signals, an alternative interpretation might be that responses simply reflect sensory bottom-up signals that are more related to some low-level stimulus characteristics than to prediction errors.

This is correct – we will expand on the discussion of this point in the manuscript.

Moreover, This interpretational uncertainty is compounded by the fact that the used experimental paradigms were not suited to test whether behaviour is impacted as a function of the visual stimulation which makes it difficult to assess what the internal representation of the animal actual was. For these reasons, the observed effects might reflect simple bottom-up sensory processing alterations and not necessarily have any functional consequences. While this potential alternative explanation does not detract from the value of the study, future work would be needed to explain the effect of antipsychotic drugs on responses to visual flow. For example, experimental designs that systematically vary the predictive strength of coupled events or that include a behavioural readout might be more suited to draw from conclusions about whether antipsychotic drugs indeed alter internal representations.

We agree that much additional work will be necessary to identify internal representation neurons. However, it is difficult to envision how behavioral output could be used to make inferences about internal representations in sensory areas of cortex. In humans, for example, there is evidence that internal representations in visual cortex and behavioral output are not always directly related: binocular rivalry activates representations of both stimuli shown in visual cortex, while the conscious experience that drives behavioral output is only of one of the two stimuli. Hence, we would assume that the internal representation in visual cortex does not necessarily relate to behavioral output.

• Methodological constraints of experimental design

While the study findings provide valuable insights into the potential effects of antipsychotic drugs, it is important to acknowledge that there may be some methodological constraints that could impact the interpretation of the results. More specifically, the experimental design does not include a negative control condition or different doses. These conditions would help to ensure that the observed effects are not due to unspecific effects related to injection-induced stress or time, and not confined to a narrow dose range that might or might not reflect therapeutic doses used in humans. Hence, future work is needed to confirm that the observed effects indeed represent specific drug effects that are relevant to antipsychotic action.

We agree that both dosages and a broader spectrum of non-antipsychotic compounds will need to be investigated. We are in the process of building a screening pipeline to perform exactly these types of experiments. We would however argue that the paper already includes a control condition in the form of the amphetamine data (Figure 7). While it is possible that amphetamine might have an effect that exactly cancels out potential i.p. injection- or stress-induced changes, we would argue it is more probable that these changes had no measurable effect on Tlx3 positive L5 IT neuron calcium activity per se. We will provide additional evidence that time or injection stress alone do not result in the observed effects.

Conclusion:

Overall, the results support the idea that antipsychotic drugs affect neural responses to predicted and unpredicted stimuli in deep layers of cortex. Although some future work is required to establish whether this observation can indeed be explained by a drug-specific effect on predictive coding, the study provides important insights into the neural underpinnings of visual processing and antipsychotic drugs, which is expected to guide future investigations on the predictive coding hypothesis of psychosis. This will be of broad interest to neuroscientists working on predictive coding in health and in disease.

Reviewer #3 (Public Review):

The study examines how different cell types in various regions of the mouse dorsal cortex respond to visuomotor integration and how antipsychotic drugs impacts these responses. Specifically, in contrast to most cell types, the authors found that activity in Layer 5 intratelencephalic neurons (Tlx3+) and Layer 6 neurons (Ntsr1+) differentiated between open loop and closed loop visuomotor conditions. Focussing on Layer 5 neurons, they found that the activity of these neurons also differentiated between negative and positive prediction errors during visuomotor integration. The authors further demonstrated that the antipsychotic drugs reduced the correlation of Layer 5 neuronal activity across regions of the cortex, and impaired the propagation of visuomotor mismatch responses (specifically, negative prediction errors) across Layer 5 neurons of the cortex, suggesting a decoupling of long-range cortical interactions.

The data when taken as a whole demonstrate that visuomotor integration in deeper cortical layers is different than in superficial layers and is more susceptible to disruption by antipsychotics. Whilst it is already known that deep layers integrate information differently from superficial layers, this study provides more specific insight into these differences. Moreover, this study provides a first step into understanding the potential mechanism by which antipsychotics may exert their effect.

Whilst the paper has several strengths, the robustness of its conclusions is limited by its questionable statistical analyses. A summary of the paper's strengths and weaknesses follow.

Strengths:

The authors perform an extensive investigation of how different cortical cell types (including Layer 2/3, 4 , 5, and 6 excitatory neurons, as well as PV, VIP, and SST inhibitory interneurons) in different cortical areas (including primary and secondary visual areas as well as motor and premotor areas), respond to visuomotor integration. This investigation provides strong support to the idea that deep layer neurons are indeed unique in their computational properties. This large data set will be of considerable interest to neuroscientists interested in cortical processing.

The authors also provide several lines of evidence that visuomotor information is differentially integrated in deep vs. superficial layers. They show that this is true across experimental paradigms of visuomotor processing (open loop, closed loop, mismatch, drifting grating conditions) and experimental manipulations, with the demonstration that Layer 5 visuomotor integration is more sensitive to disruption by the antipsychotic drug clozapine, compared with cortex as a whole.

The study further uses multiple drugs (clozapine, aripiprazole and haloperidol) to bolster its conclusion that antipsychotic drugs disrupt correlated cortical activity in Layer 5 neurons, and further demonstrates that this disruption is specific to antipsychotics, as the psychostimulant amphetamine shows no such effect.

In widefield calcium imaging experiments, the authors effectively control for the impact of hemodynamic occlusions in their results, and try to minimize this impact using a crystal skull preparation, which performs better than traditional glass windows. Moreover, they examine key findings in widefield calcium imaging experiments with two-photon imaging.

Weaknesses:

A critical weakness of the paper is its statistical analysis. The study does not use mice as its independent unit for statistical comparisons but rather relies on other definitions, without appropriate justification, which results in an inflation of sample sizes.

We will expand on both analyses and justifications throughout.

For example, in Figure 1, independent samples are defined as locomotion onsets, leading to sample sizes of approx. 400-2000 despite only using 6 mice for the experiment. This is only justified if the data from locomotion onsets within a mouse is actually statistically independent, which the authors do not test for, and which seems unlikely. With such inflated sample sizes, it becomes more likely to find spurious differences between groups as significant. It also remains unclear how many locomotion onsets come from each mouse; the results could be dominated by a small subset of mice with the most locomotion onsets. The more disciplined approach to statistical analysis of the dataset is to average the data associated with locomotion onsets within a mouse, and then use the mouse as an independent unit for statistical comparison. A second example, for instance, is in Figure 2L, where the independent statistical unit is defined as cortical regions instead of mice, with the left and right hemispheres counting as independent samples; again this is not justified. Is the activity of cortical regions within a mouse and across cortical hemispheres really statistically independent? The problem is apparent throughout the manuscript and for each data set collected.

This may partially be a misunderstanding. Figures 1F-1K indeed use locomotion onsets as a unit, but there were no statistical comparisons. In these Figures we were addressing the question of whether locomotion onsets in closed loop differ from those in open loop. Thus, we quantify variability as a unit of locomotion onsets. The question of mouse-to-mouse variability of this analysis is a slightly different one. We did include the same analysis (for visual cortex) with the variability calculated across mice as Figure S2. We will expand this supplementary figure with the equivalent data of Figure 3 to further address this concern.

For Figure 1L (we assume the reviewer means Figure 1L, not Figure 2L), the unit we used for analysis was cortical area. We will update and improve the analysis. This was indeed not optimal, and we will replace the statistical testing with hierarchical bootstrap (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC7906290/) to account for nested data.

An additional statistical issue is that it is unclear if the authors are correcting for the use of multiple statistical tests (as in for example Figure 1L and Figure 2B,D). In general, the use of statistics by the authors is not justified in the text.

We will update and improve the analysis shown in Figure 1L.

In Figures 2B and 2D, we think adding family-wise error correction would be slightly misleading. We could add a correction – our conclusions would remain unchanged almost independent of the choice of correction (most of the significant p values are infinitesimally small, see Table S1). However, our interpretation is not focusing on one particular comparison (of many possible comparisons) that is significant - all comparisons between closed and open loop data points were significant in the L5 IT recordings and none of them were significant in the recordings in C57BL/6 mice that expressed GCaMP brain-wide.

Finally, it is important to note that whilst the study demonstrates that antipsychotics may selectively impact visuomotor integration in L5 neurons, it does not show that this effect is necessary or sufficient for the action of antipsychotics; though this is likely beyond the scope of the study it is something for readers to keep in mind.

We fully agree, it is still unclear how the effects we observe in our work relate to the treatment relevant effects in patients. We will expand on this point in the discussion.

The idea here focuses a lot on memory retention of past events which I think can be approached in two ways:

1. At the level of the EDR itself: just like Dinil already suggested, instead of simply checking a threshold of maliciousness, we can monitor the gradient as well to effectively raise signals with an increasing maliciousness of event sequences. The idea of aggregated events across boots or even distributed analysis across similar clients also fit into this scenario

2. At the ML level using such architectures as LSTMs, attention layers, memory based graph networks, etc.

We may need to use both approaches here

I agree with this statement. There are so many factors to consider when creating something that is to be used by various kinds of people. It may feel as though it is fair in the moment, but we need to stop and think of whether we missed anything or disregarded a disability because we ourselves do not have it.

Author Response:

Assessment note: “Whereas the results and interpretations are generally solid, the mechanistic aspect of the work and conclusions put forth rely heavily on in vitro studies performed in cultured L6 myocytes, which are highly glycolytic and generally not viewed as a good model for studying muscle metabolism and insulin action.”

While we acknowledge that in vitro models may not fully recapitulate the complexity of in vivo systems, we believe that our use of L6 myotubes is appropriate for studying the mechanisms underlying muscle metabolism and insulin action. As mentioned below (reviewer 2, point 1), L6 myotubes possess many important characteristics relevant to our research, including high insulin sensitivity and a similar mitochondrial respiration sensitivity to primary muscle fibres. Furthermore, several studies have demonstrated the utility of L6 myotubes as a model for studying insulin sensitivity and metabolism, including our own previous work (PMID: 19805130, 31693893, 19915010).

In addition, we have provided evidence of the similarities between L6 cells overexpressing SMPD5 and human muscle biopsies at protein levels and the reproducibility of the negative correlation between ceramide and Coenzyme Q observed in L6 cells in vivo, specifically in the skeletal muscle of mice in chow diet. These findings support the relevance of our in vitro results to in vivo muscle metabolism.

Finally, we will supplement our findings by demonstrating a comparable relationship between ceramide and Coenzyme Q in mice exposed to a high-fat diet, to be shown in Supplementary Figure 4 H-I. Further animal experiments will be performed to validate our cell-line based conclusions. We hope that these additional results address the concerns raised by the reviewer and further support the relevance of our in vitro findings to in vivo muscle metabolism and insulin action.

Points from reviewer 1:

1. Although the authors' results suggest that higher mitochondrial ceramide levels suppress cellular insulin sensitivity, they rely solely on a partial inhibition (i.e., 30%) of insulin-stimulated GLUT4-HA translocation in L6 myocytes. It would be critical to examine how much the increased mitochondrial ceramide would inhibit insulin-induced glucose uptake in myocytes using radiolabel deoxy-glucose.

Response: The primary impact of insulin is to facilitate the translocation of glucose transporter type 4 (GLUT4) to the cell surface, which effectively enhances the maximum rate of glucose uptake into cells. Therefore, assessing the quantity of GLUT4 present at the cell surface in non-permeabilized cells is widely regarded as the most reliable measure of insulin sensitivity (PMID: 36283703, 35594055, 34285405). Additionally, plasma membrane GLUT4 and glucose uptake are highly correlated. Whilst we have routinely measured glucose uptake with radiolabelled glucose in the past, we do not believe that evaluating glucose uptake provides a better assessment of insulin sensitivity than GLUT4.

We will clarify the use of GLUT4 translocation in the Results section:

“...For this reason, several in vitro models have been employed involving incubation of insulin sensitive cell types with lipids such as palmitate to mimic lipotoxicity in vivo. In this study we will use cell surface GLUT4-HA abundance as the main readout of insulin response...”

1. Another important question to be addressed is whether glycogen synthesis is affected in myocytes under these experimental conditions. Results demonstrating reductions in insulin-stimulated glucose transport and glycogen synthesis in myocytes with dysfunctional mitochondria due to ceramide accumulation would further support the authors' claim.

Response: We have carried out supplementary experiments to investigate glycogen synthesis in our insulin-resistant models. Our approach involved L6-myotubes overexpressing the mitochondrial-targeted construct ASAH1 (as described in Fig. 3). We then challenged them with palmitate and measured glycogen synthesis using 14C radiolabeled glucose. Our observations indicated that palmitate suppressed insulin-induced glycogen synthesis, which was effectively prevented by the overexpression of ASAH1 (N = 5, * p<0.05). These results provide additional evidence highlighting the role of dysfunctional mitochondria in muscle cell glucose metabolism.

These data will be added to Supplementary Figure 4K and the results modified as follows:

“Notably, mtASAH1 overexpression protected cells from palmitate-induced insulin resistance without affecting basal insulin sensitivity (Fig. 3E). Similar results were observed using insulin-induced glycogen synthesis as an ortholog technique for Glut4 translocation. These results provide additional evidence highlighting the role of dysfunctional mitochondria in muscle cell glucose metabolism (Sup. Fig. 5K). Importantly, mtASAH1 overexpression did not rescue insulin sensitivity in cells depleted…”

We will add to the method section:

“L6 myotubes overexpressing ASAH were grown and differentiated in 12-well plates, as described in the Cell lines section, and stimulated for 16 h with palmitate-BSA or EtOH-BSA, as detailed in the Induction of insulin resistance section.

On day seven of differentiation, myotubes were serum starved in plain DMEM for 3 and a half hours. After incubation for 1 hour at 37C with 2 µCi/ml D-[U-14C]-glucose in the presence or absence of 100 nM insulin, glycogen synthesis assay was performed, as previously described (Zarini S. et al., J Lipid Res, 63(10): 100270, 2022).”

1. In addition, it would be critical to assess whether the increased mitochondrial ceramide and consequent lowering of energy levels affect all exocytic pathways in L6 myoblasts or just the GLUT4 trafficking. Is the secretory pathway also disrupted under these conditions?

Response: As the secretory pathway primarily involves the synthesis and transportation of soluble proteins that are secreted into the extracellular space, and given that the majority of cellular transmembrane proteins (excluding those of the mitochondria) use this pathway to arrive at their ultimate destination, we believe that the question posed by the reviewer is highly challenging and beyond the scope of our research. We will add this to the discussion:

“...the abundance of mPTP associated proteins suggesting a role of this pore in ceramide induced insulin resistance (Sup. Fig. 6E). In addition, it is yet to be determined whether the trafficking defect is specific to Glut4 or if it affects the exocytic-secretory pathway more broadly…”

Points from reviewer 2:

1. The mechanistic aspect of the work and conclusions put forth rely heavily on studies performed in cultured myocytes, which are highly glycolytic and generally viewed as a poor model for studying muscle metabolism and insulin action. Nonetheless, the findings provide a strong rationale for moving this line of investigation into mouse gain/loss of function models.

Response: The relative contribution of the anaerobic (glycolysis) and aerobic (mitochondria) contribution to the muscle metabolism can change in L6 depending on differentiation stage. For instance, Serrage et al (PMID30701682) demonstrated that L6-myotubes have a higher mitochondrial abundance and aerobic metabolism than L6-myoblasts. Others have used elegant transcriptomic analysis and metabolic characterisation comparing different skeletal muscle models for studying insulin sensitivity. For instance, Abdelmoez et al in 2020 (PMID31825657) reported that L6 myotubes exhibit greater insulin-stimulated glucose uptake and oxidative capacity compared with C2C12 and Human Mesenchymal Stem Cells (HMSC). Overall, L6 cells exhibit higher metabolic rates and primarily rely on aerobic metabolism, while C2C12 and HSMC cells rely on anaerobic glycolysis. It is worth noting that L6 myotubes are the cell line most closely related to adult human muscle when compared with other muscle cell lines (PMID31825657). Our presented results in Figure 6 H and I provide evidence for the similarities between L6 cells overexpressing SMPD5 and human muscle biopsies. Additionally, in Figure 3J-K, we demonstrate the reproducibility of the negative correlation between ceramide and Coenzyme Q observed in L6 cells in vivo, specifically in the skeletal muscle of mice in chow diet. Furthermore, we have supplemented these findings by demonstrating a comparable relationship in mice exposed to a high-fat diet, as shown in Supplementary Figure 4 H-I (refer to point 4). We will clarify these points in the Discussion:

“In this study, we mainly utilised L6-myotubes, which share many important characteristics with primary muscle fibres relevant to our research. Both types of cells exhibit high sensitivity to insulin and respond similarly to maximal doses of insulin, with Glut4 translocation stimulated between 2 to 4 times over basal levels in response to 100 nM insulin (as shown in Fig. 1-4 and (46,47)). Additionally, mitochondrial respiration in L6-myotubes have a similar sensitivity to mitochondrial poisons, as observed in primary muscle fibres (as shown in Fig. 5 (48)). Finally, inhibiting ceramide production increases CoQ levels in both L6-myotubes and adult muscle tissue (as shown in Fig. 2-3). Therefore, L6-myotubes possess the necessary metabolic features to investigate the role of mitochondria in insulin resistance, and this relationship is likely applicable to primary muscle fibres”.

We will also add additional data - in point 2 - from differentiated human myocytes that are consistent with our observations from the L6 models. Additional experiments are in progress to further extend these findings.

1. One caveat of the approach taken is that exposure of cells to palmitate alone is not reflective of in vivo physiology. It would be interesting to know if similar effects on CoQ are observed when cells are exposed to a more physiological mixture of fatty acids that includes a high ratio of palmitate, but better mimics in vivo nutrition.

Response: Palmitate is widely recognized as a trigger for insulin resistance and ceramide accumulation, which mimics the insulin resistance induced by a diet in rodents and humans. Previous studies have compared the effects of a lipid mixture versus palmitate on inducing insulin resistance in skeletal muscle, and have found that the strong disruption in insulin sensitivity caused by palmitate exposure was lessened with physiologic mixtures of fatty acids, even with a high proportion of saturated fatty acids. This was associated, in part, to the selective partitioning of fatty acids into neutral lipids (such as TAG) when muscle cells are exposed to physiologic lipid mixtures (Newsom et al PMID25793412). Hence, we think that using palmitate is a better strategy to study lipid-induced insulin resistance in vitro. We will add to results:

“In vitro, palmitate conjugated with BSA is the preferred strategy for inducing insulin resistance, as lipid mixtures tend to partition into triacylglycerides (33)”.

We are also performing additional in vivo experiments to add to the physiological relevance of the findings.

1. While the utility of targeting SMPD5 to the mitochondria is appreciated, the results in Figure 5 suggest that this manoeuvre caused a rather severe form of mitochondrial dysfunction. This could be more representative of toxicity rather than pathophysiology. It would be helpful to know if these same effects are observed with other manipulations that lower CoQ to a similar degree. If not, the discrepancies should be discussed.

Response: We conducted a staining procedure using the mitochondrial marker mitoDsRED to observe the effect of SMPD5 overexpression on cell toxicity. The resulting images, displayed in the figure below (Author Response Figure 1), demonstrate that the overexpression of SMPD5 did not result in any significant changes in cell morphology or impact the differentiation potential of our myoblasts into myotubes.

Author Response Figure 1.

In addition, we evaluated cell viability in HeLa cells following exposure to SACLAC (2 uM) to induce CoQ depletion (left panel). Specifically, we measured cell death by monitoring the uptake of Propidium iodide (PI) as shown in the right panel. Our results demonstrated that Saclac-induced CoQ depletion did not lead to cell death at the doses used for CoQ depletion (Author Response Figure 2).

Author Response Figure 2.

Therefore, we deemed it improbable that the observed effect is caused by cellular toxicity, but rather represents a pathological condition induced by elevated levels of ceramides. We will add to discussion:

“...downregulation of the respirasome induced by ceramides may lead to CoQ depletion. Despite the significant impact of ceramide on mitochondrial respiration, we did not observe any indications of cell damage in any of the treatments, suggesting that our models are not explained by toxic/cell death events.”

1. The conclusions could be strengthened by more extensive studies in mice to assess the interplay between mitochondrial ceramides, CoQ depletion and ETC/mitochondrial dysfunction in the context of a standard diet versus HF diet-induced insulin resistance. Does P053 affect mitochondrial ceramide, ETC protein abundance, mitochondrial function, and muscle insulin sensitivity in the predicted directions?

Response: We would like to note that the metabolic characterization and assessment of ETC/mitochondrial function in these mice (both fed a high-fat (HF) and chow diet, with or without P053) were previously published (Turner N, PMID30131496). In addition to this, we have conducted targeted metabolomic and lipidomic analyses to investigate the impact of P053 on ceramide and CoQ levels in HF-fed mice. As illustrated in the figures below (Author Response Figure 3), the administration of P053 led to a reduction in ceramide levels (left panel) and an increase in CoQ levels (right panel) in HF-fed mice, which is consistent with our in vitro findings.

Author Response Figure 3.

We will add to results:

“…similar effect was observed in mice exposed to a high fat diet for 5 wks (Supp. Fig. 4H-I further phenotypic and metabolic characterization of these animals can be found in (41))”

We will further perform more in-vivo studies to corroborate these findings.

Having the internet swarmed by generative agents is unlike current bots and scripts. It will be harder to see diff between humans and machines online. This may be problematic for those of us who treat the web as a space for human interaction.

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

Learn more at Review Commons

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Reply to the reviewers

We thank the reviewers for their comments and constructive suggestions to improve the manuscript. We are encouraged to see that both reviewers acknowledge how the results from our manuscript uses state-of-art technologies to advance molecular underpinnings of centriole length, integrity and function regulation. Both reviewers also highlighted that the manuscript is well laid out and presents clear, rigorous, and convincing data. Reviewer#1 described our manuscript of highest experimental quality and broad interest to the field of centrosome and cell biology form a basic research and genetics/clinical point of view. Here, we explain the revisions, additional experimentations and analyses planned to address the points raised by the referees. We will perform most of the experimentations and corrections requested by the reviewers. We have already made several revisions and are currently working on additional experiments.

Our responses to each reviewer comment in bold are listed below. References mentioned here are listed in the references section included at the of this document.

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

Summary: __In this manuscript, Arslanhan and colleagues use proximity proteomics to identify CCDC15 as a new centriolar protein that co-localizes and interacts with known inner scaffold proteins in cell culture-based systems. Functional characterization using state-of-the-art expansion microscopy techniques reveals defects in centriole length and integrity. The authors further reveal intriguing aberrations in the recruitment of other centriole inner scaffold proteins, such as POC1B and the SFI1/centrin complex, in CCDC15-deficient cells, and observe defects in primary cilia. __

We thank the reviewer for the accurate summary of the major conclusions of our manuscript.

Major points:

1) The authors present a high-quality manuscript that identifies a novel centriolar protein by elegantly revealing and comparing the proximity proteomes of two known centriolar proteins, which represents an important component for the maintenance of centrioles.

We thank the reviewer for highlighting that our manuscript is of high quality and presents important advances for the field.

__2) Data are often presented from two independent experiments (n = 2), which is nice, but also the minimum for experiments in biology. It is strongly recommended to perform at least three independent experiments. __

We agree with the reviewer that analysis of data form three experimental replicates is ideal for statistical analysis. We performed three replicates for the majority of experiments in the manuscript. However, as the reviewer pointed out, we included analysis from two experiments for the following figures:

• Fig. 4H: quantification of CCDC15 total cellular levels throughout the cell cycle by western blotting
• Fig. 5A: CCDC15-positive centrioles in control and CCDC15 siRNA-transfected cells
• Fig. 6B: % centriolar coverage of POC5, FAM161A, POC1B and Centrin-2 in control and CCDC15 siRNA-transfected cells
• Fig. 6C, 6E: Centrin-2 or SFI1-positive centrioles in control and CCDC15 siRNA-transfected cells
• Fig. 6J, K: normalized tubulin length and percentage of defective centrioles in cells depleted for CCDC15 or co-depleted for CCDC15 and POC1B
• Fig. 7F, H: SMO-positive cilia and basal body IFT88 levels in control and CCDC15 siRNA-transfected cells
• Fig. S3H: centriole amplification in HU-treated control and CCDC15 siRNA-transfected cells (no)
• Fig. S3A: centrosomal levels upon CCDC15 depletion There are two reasons for why we performed two experimental replicates for these experiments: 1) results from the two experimental replicates were similar, 2) quantification of data by U-ExM is laborious. To address the reviewer’s comments, we will perform the third experimental replicate for the sets of data that led to major conclusions of our manuscript, which are Figures 4H, 6C, 6E, 6J, 6K, 7F, 7H and S3A.

3) The protein interaction studies presented in Fig. 3 could be of higher quality. While it is great that the authors compared interactions to the centriolar protein SAS6, which is not expected to interact with CCDC15, the presented data raise many questions.

__a) In most cases, co-expression of tagged CCDC15 stabilizes the tested interaction partners, such that the overall abundance seems to be higher. The increase in protein abundance is substantial for Flag-FAM161A (Fig. 3D) and GFP-Centrin-2 (Fig. 3E) and is even higher for the non-interactor SAS6 (Fig. 3G), while it cannot be assessed for GFP-POC1B (Fig. 3F). Hence, the higher expression levels under these conditions make it more likely that these proteins are "pulled down" and therefore do not represent appropriate controls. __

We agree with the reviewer that the differences in protein abundance of the prey proteins upon expression of CCDC15 relative to control might impact the interpretation of the interaction data. To address this concern, we will perform the following experiments:

• To account of the potential stabilizing effects of CCDC15 expression, we will change the relative ratio of plasmids expressing proteins of interest and assess the expression of bait and prey protein levels. We will then repeat the co-immunoprecipitation experiments in conditions where prey expression levels are similar.
• To avoid the potential stabilizing effects of CCDC15 overexpression, we will perform immunoprecipitation experiments in cells expressing GFP or V5-tagged inner scaffold proteins and assess their potential physical or proximity interaction by blotting for endogenous CCDC15. __b) All Co-IP experiments are lacking negative controls in the form of proteins that are not pulled down under the presented conditions. __

For the co-IP experiments, we only included a specificity control for the interaction of the bait protein with the tag of the prey protein (i.e. GBP pulldown of GFP or GFP-CCDC15-expressing cells). As the reviewer suggested, we will also include a specificity control for the interaction of bait with the tag of the prey protein for co-immunoprecipitation experiments (i.e. GFP pulldown of cells expressing GFP-CCDC15 with V5-BirA* or V5-BirA*-FAM161A).

__c) The amounts of co-precipitation of the tested proteins appears very different. Could this reflect strong or weak interactors, or does it reflect the abundance of the respective proteins in centrioles? __

We agree with the reviewer that the quantity of the co-precipitated prey proteins might be a proxy for the interaction strength if the abundance of the bait proteins is similar. However, the expression levels of bait and prey proteins in co-transfected cells are different and thus, cannot be used to derive a conclusion on the interaction strength. For the revised manuscript, we will repeat the IP experiments and comment on this in the discussion section.

__4) The observation that IFT88 is supposedly decreased at the base of cilia in CCDC15-depleted cells requires additional experiments/evidence. Fig. 7G shows the results of n = 2 and more importantly, a similar reduction of gamma-tubulin in siCCDC15. Could the observed reduction in IFT88 be explained by a decrease in accessibility to immunofluorescence microscopy? Would the reduction in IFT88 at the base also be apparent when the signals were normalized to gamma-tubulin signals? __

To address the reviewer’s concern, we quantified the basal body gamma-tubulin and IFT88 levels in control and CCDC15-depleted cells and plotted the basal body IFT88 levels normalized to gamma-tubulin levels in Fig. 7H. Similar to the reduction in IFT88 levels, gamma-tubulin-normalized IFT88 levels was significantly less relative to control cells. Moreover, the gamma-tubulin basal body levels were similar between control and CCDC15 cells. We revised the gamma-tubulin micrographs in Fig. 7G to represent this. These results indicate that the reduction in basal body IFT88 levels upon CCDC15 depletion in specific.

__5) The observed Hedgehog signaling defects are described as follows: "CCDC15 depletion significantly decreased the percentage of SMO-positive cells". It is similarly described in the figure legend. If this was true, the simplest explanation would be that it reflects the reduction in ciliation rate (which is in a similar range). If SMO-positive cilia (instead of "cells") were determined, the text needs to be changed accordingly. __

As the reviewer pointed out, we quantified SMO-positive cilia, but not cells. We are sorry for this typo. We corrected SMO-positive cells as SMO-positive cilia in the manuscript text, Fig. 7 and figure legends.

__6) OPTIONAL: While expansion microscopy is slowly becoming one of the standard super-resolution microscopy methods, which is particularly well validated for studying centrioles, the authors should consider confirming part of their findings (as a proof of principle, surely not in all instances) by more established techniques. This could serve to convince critical reviewers that may argue that the expansion process may induce architectural defects of destabilized centrioles, as observed after disruptions of components, such as in Fig. 6. Alternatively, the authors could cite additional work that make strong cases about the suitability of expansion microscopy for their studies, ideally with comparisons to other methods. __

• SIM imaging was previously successfully applied for nanoscale mapping of other centriole proteins including CEP44, MDM1 and PPP1R35 (Atorino et al., 2020; Sydor et al., 2018; Van de Mark et al., 2015). To complement the U-ExM analysis, we have started imaging cells stained for CCDC15 and different centriole markers (i.e. distal appendage, proximal linker, centriole wall) using a recently purchased 3D-SIM superresolution microscope. We already included the SIM imaging data for CCDC15 localization in centrosome fractions purified from HEK293T cells in Fig. S5B. In the revised manuscript, we will replace confocal imaging data in Fig. 3A and 3B with SIM imaging data.
• As the reviewer noted, expansion microscopy has been successfully used for the analysis of a wide range of cellular structures and scientific questions including nanoscale mapping of cellular structures across different organisms. In particular, U-ExM of previously characterized centrosome proteins various centriole proteins have significantly advanced our understanding of centriole ultrastructure. In our manuscript, we used the U-ExM protocol that was validated for centrioles by comparative analysis of U-ExM and cryo-ET imaging by our co-authors (Gambarotto et al., 2019; Hamel et al., 2017). To clarify these points, we included the following sentence along with the relevant references in the introduction: “Application of the U-ExM method to investigate known centrosome proteins has started to define the composition of the inner scaffold as well as other centriolar sub-compartments (Chen et al., 2015; Gambarotto et al., 2021; Gambarotto et al., 2019; Kong and Loncarek, 2021; Laporte et al., 2022; Mahen, 2022; Mercey et al., 2022; Odabasi et al., 2023; Sahabandu et al., 2019; Schweizer et al., 2021; Steib et al., 2022; Tiryaki et al., 2022; Tsekitsidou et al., 2023).”

Minor points:

1) Text, figures, and referencing are clear and accurate, apart from minor exceptions.

We clarified and corrected the points regarding text, figures and references as suggested by the two reviewers.

__ 2) The title suggests a regulator role for CCDC15 in centriole integrity and ciliogenesis, which has formally not been shown. __

We revised the title as “CCDC15 localizes to the centriole inner scaffold and functions in centriole length control and integrity”.

__3) As the authors observe changes in centriole lengths in the absence of CCDC15, it would be very insightful to compare these phenotypes to other components that affect centriolar length, such as C2CD3, human Augmin complex components (as HAUS6 is identified in Fig. 1) or others. These could be interesting aspects for discussion, additional experiments are OPTIONAL. __

We agree with the reviewer that comparative analysis of centriole length phenotypes for CCDC15 and other components that regulate centriole length will provide insight into how these components work together at the centriole inner core. To this end, we phenotypically compared CCDC15 loss-of-function phenotypes to that of other components of the inner scaffold (POC5, POC1B, FAM161A) that interact with CCDC15. In agreement with their previously reported functions in U2OS or RPE1 cells, we found that POC5 depletion resulted in a 4% slight but significant increase in centriole length and POC1B depletion resulted in a 15% significant decrease. In contrast, FAM161A depletion did not alter centriole length (siControl: 447.8±59.7 nm, siFAM161A 436.3±64 nm). Together, our analysis of their centriolar localization dependency and regulatory roles during centriole length suggest that CCDC15 and POC1B might form a functional complex as positive regulators of centriole length. In contrast, POC5 functions as a negative regulator and might be part of a different pathway for centriole length regulation. We integrated the following sub-paragraph in the results section and also included discussion of this data in the discussion section:

“Moreover, we quantified centriole length in control cells and cells depleted for POC5 or POC1B. While POC5 depletion resulted in longer centrioles, POC1B resulted in shorter centrioles (POC5: siControl: 414.1 nm±38.3, siPOC5: 432.7±44.8 nm, POC1B: siControl: 400.6±36.1 nm, siPOC1B: 341.5±44.39 nm,). FAMA161A depletion did not alter centriole length (siControl: 447.8±59.7 nm, siFAM161A 436.3±64 nm). Together, these results suggest that CCDC15 might cooperate with POC1B and compete with POC5 to establish and maintain proper centriole length.”

__ 4) While the reduced ciliation rate in the absence of CCDC15 is convincing, the authors did not investigate "ciliogenesis", i.e. the formation of cilia, and hence should re-phrase. The sentence in the discussion that "CCDC15 functions during assembly" should be removed. __

To clarify that we only investigated the role of CCDC15 in the ability of cells to form cilia, we replaced sentences that indicates “CCDC15 functions in cilium assembly” with “CCDC15 is required for the efficiency of cilia formation”.

__5) The existence of stably associated CCDC15 pools with centrosomes (Fig. 2) requires further evidence. The recovery of fluorescence after photobleaching in FRAP experiments is strongly dependent on experimental setups and is only semi-quantitative. A full recovery is unrealistic, hence, it is ideally compared to a known static or known mobile component. I personally think this experiment -as it is presented now- is of little value to the overall fantastic study. The authors may consider omitting this piece of data. __

We agree with the reviewer that FRAP data by itself does not prove the existence of stably associated CCDC15 pool. As controls in these experiments, we use FRAP analysis of GFP-CCDC66, which has a 100% immobile pool at the cilia and 50% immobile pool at the centrosomes as assessed by FRAP (Conkar et al., 2019). To address these points, we toned down the conclusions derived from this experiment by revising the sentence as follows:

Additionally, we note that the following data provides support for the stable association of CCDC15 at the centrioles:

• About 49.6% (± 3.96) of the centrioles still had CCDC15 fluorescence signal at one of the centrioles upon CCDC15 siRNA treatment (Fig. 5A, 5B). The inefficient depletion of the mature centriole pool of CCDC15 is analogous to what was observed upon depletion of other centriole lumen and inner scaffold proteins including WDR90 and HAUS6 (Schweizer et al., 2021; Steib et al., 2020). __6) The data that CCDC15 is a cell cycle-regulated protein is not very convincing (see Fig. 3H), as the signals area weak and the experiment has been performed only once (n= 1). This piece of data does not appear to be very critical for the main conclusions of the manuscript and may be omitted. Otherwise, this experiment should be repeated to allow for proper statistical analysis. __

We will perform these experiments two more times, quantify cellular abundance of CCDC15 in synchronized populations from three experimental replicates and plot it with proper statistical analysis.

__7) Experimental details on how "defective centrioles" are determined are missing. __

We included the following experimental details to the methods section:

“Centrioles were considered as defective when the roundness of the centriole was lost or the microtubule walls were broken or incomplete. In the longitudinal views of centrioles, defective centrioles were visualized as heterogenous acetylated signal along the centriole wall or irregularities in the cylindrical organization of the centriole wall (Fig. 5F). We clarified these points in the methods section.

__ 8) For figures, in which the focus should be on growing centrioles (see Fig. 4), it could be helpful to guide the reader and indicate the respective areas of the micrographs by arrows. __

We added arrows to point to the respective areas of the micrographs in Fig. 4F.

__ 9) Page18: "centriole length shortening" could be changed to "centriole shortening". __

We corrected this description as suggested.

__10) It is unclear how the authors determine distal from proximal ends of centrioles in presented micrographs (see Fig. 5D). __

We determined the proximal and distal ends of the centrioles by taking the centriole pairs as a proxy. Even though we only represent a micrograph containing a single centriole in some of the U-ExM figures including Fig. 5D, the uncropped micrographs contain two centrioles, which are oriented orthogonally and tethered to each other at their proximal ends in interphase cells. We added the following sentence to the methods section to clarify this point:

*“Since centrioles are oriented orthogonally and tethered to each other at their proximal ends in interphase cells, we also used the orientation of the centriole pairs as a proxy to determine the proximal and distal ends of the centrioles.” *

__11) Fig. 7A is missing scale bars and Fig.7 overall is lacking rectangle indicators of the areas that are shown at higher magnification in the insets. __

We added scale bar to Fig. 7A and rectangle indicators for zoomed in regions in Fig. A, E, G.

12) Fig. 7C displays cilia that appear very short, especially when comparing to the micrographs and bar graphs presented. The authors may want to explain this discrepancy.

We thank the reviewer for the comment. The zoomed in representative cilia is 4.1 µM in control cells and 1.4 µM in CCDC15-depleted cells. Therefore, the representative cilia is in agreement with the quantification of cilia in Fig. 7C.

Reviewer #1 (Significance (Required)): • From a technical point of view the authors use two state-of-the-art technologies, namely proximity labeling combined with proteomics and ultrastructure expansion microscopy, that are both challenging and very well suited to address the main questions of this study. ____ • General assessment: The presented study is of highest experimental quality. Despite being very challenging, the expansion microscopy and proximity proteomics experiments have been designed and performed very well to allow solid interpretation. The results of the central data are consistent and allow strong first conclusions about the putative function of the newly identified centriolar protein CCDC15. The study presents a solid foundation for future hypothesis-driven, mechanistic analysis of CCDC15 and inner scaffold proteins in centriole length control and maintaining centriole integrity. The only limitation of the study is that the technically simpler experiments should be repeated to allow proper statistical assessment, which can be addressed easily. • Advance: This is the first study that identifies CCDC15 as a centriolar protein and localizes it to the inner scaffold. It further describes a function for CCDC15 in centriole length control and shows its importance in maintaining centriole integrity with consequences for stable cilia formation in tissue culture. The study provides further functional insights into the interdependence of inner scaffold proteins and the role of CCDC15 in the recruitment of the SFI1/centrin distal complex. • Audience: The manuscript will be of broad interest to the fields of centrosome and cell biology, both from a basic research and genetics/clinical point of view due to the association with human disorders. The state-of-the-art technologies applied will be of interest to a broader cell and molecular biology readership that studies subcellular compartments and microtubules. • Reviewer's field of expertise: Genetics, imaging, and protein-protein interaction studies with a focus on centrosomes and cilia.

We thank the reviewer for recognizing the importance of our work and for supportive and insightful comments that will further strengthen the conclusions of our manuscript. Our planned revisions will address the only major technical limitation raised by the reviewer that requires adding one more experimental replicate for analysis of the data detailed in major point#1. Notably, we also thank the reviewer to specifying the experiments that are not essential or will be out of the scope of our manuscript as “optional”.

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

Summary:

__In this study, Arslanhan et al. propose CCDC15 as a novel component of the centriole inner scaffold structure with potential roles in centriole length control, stability and the primary cilium formation in cultured epithelial cells. Using proximity labelling they explore the common interactors of Poc5 and Centrin-2, two resident molecules of the centriole inner scaffold, to hunt for novel regulators of this structure. The authors leverage expansion microscopy-based localization and siRNA-dependent loss-of-function experiments to follow up on one such protein they identify, CCDC15, with the aforementioned roles in centriole and cilia biology.

This study is designed and laid out nicely; however, to be able to support some of the important claims regarding their proximity labelling results and exploration on the roles of CCDC15, there are several major technical and reproducibility concerns that deem major revision. Similarly, the introduction (perhaps inadvertently) omits much of the recent studies on centriole size control that have highlighted the complexity of this biological problem. As such, addressing the following major points will be essential in further considering this work for publication. __

__We thank the reviewer for recognizing the importance of our work and appreciate the positive reflections on our manuscript and the feedback comments that were well thought-out and articulated and will further strengthen the conclusions of our manuscript. Our planned revisions focus on addressing the reviewer’s comments especially in further supporting our conclusions for proximity-labeling, phenotypic characterization and immunoprecipitation experiments, examining CCDC15 centriole localization in an additional cell line and investigating how CCDC15 works together during centriole length control with known components of the inner scaffold. __

Major points:

__1a) The authors use Poc5 and Centrin-2 molecules as joint baits to reveal the interactome of the centriole inner scaffold, however the work lacks appropriate experimental and analytical controls to argue that this is a proximity mapping "at the centriole inner scaffold". In its current state, it is simply an interactome of total Poc5 and Centrin-2, and it might be misleading to call it an interactome at the centriole inner scaffold (the statistical identification of shared interactors cannot do full justice to their biology at the centrosome). Appropriate expression data needed to delineate how large the centrosomal vs. cytoplasmic (or nucleoplasmic) fraction is for either of these molecules, both without and upon the addition of biotin (to see whether the bulk of interaction data stem from the cytoplasm/nucleoplasm or the centrioles themselves). The authors can test this by selectively blotting a lysate fraction containing the centrosomes after centrifugation, and compare them with the simultaneous blot of the supernatant (which were readily used for the blots presented in Fig. 1B). This experiment also becomes very relevant for the case of Centrin-2, as it also heavily localizes to the nucleoplasm as the authors found out (see Fig. 1A and Fig. S1A). __

__ Additionally, an orthogonal approach should be taken to perform bio-image analysis on their biotin/streptavidin imaging data to demonstrate the exact ratios between the centrosomal vs. cytoplasmic/nucleoplasmic biotin activation with appropriate signal normalization between the biotin/streptavidin images. This is particularly important, as although the authors claim that these cells stably express the V5BirA*, it seems that there is partial clonality to the expression. Some cells in both the Poc5 and Centrin-2 fusion constructs appear to lack the V5/Streptavidin signals upon Biotin addition (such as the two cells in the centre right in Poc5, and again a cell in the centre right for Centrin-2 images). In its current form, Fig. 1A lacks signal quantification and does not report any information about the replicates and distributions of the data. I worry that this may raise concerns on the reproducibility if published in its current form. __a) We agree with the reviewer that the proximity maps of POC5 and

a) Centrin-2 are not specific to the centriole inner scaffold and thus, do not represent the inner scaffold interactome. The proximity maps identified interactions across different pools of POC5 and Centrin-2 in nucleus, cytoplasm and centrosomes (Fig. 1, S1). To highlight these important points, we already included extensive analysis of the different cellular compartments and biological processes identified by the POC5 and Centrin-2 proximity maps in the results section (pg. 9-10).

We think that there are two reasons that caused the misinterpretation of the use of these proximity maps as the “inner scaffold interactome”: 1) the way we introduced the motivation for proximity mapping studies, 2) proposing the use of the resulting interactomes as resources for identification of the full repertoire of the inner scaffold proteins. To clarify these points, we revised the manuscript in all relevant parts that might have led to misinterpretation. Following are the specific revisions:

• To clarify that the proximity maps are not specific to the inner scaffold pools of POC5 and Centrin-2, we revised the title of the results section for Fig. 1 and 2 as follows: “Proximity mapping of POC5 and Centrin-2 identifies new centriolar proteins”.

• To indicate that POC5 and Centrin-2 localizes to the cytoplasm and/or nucleus in addition to the centrosome, we added the following sentence to the result section: “In addition to centrosomes, both fusion proteins also localized to and induced biotinylation diffusely in the cytoplasm and/or nucleus (Fig. 1A).”

• In the introduction, we revised the following sentence “Here, we used the known inner scaffold proteins as probes to identify the molecular makeup of the inner scaffold in an unbiased way.” as follows: *“Here, we used the known inner scaffold proteins as probes to identify new components of the inner scaffold”. *

• To highlight the different cellular pools of POC5 and Centrin-2 and identification of their interactors in these pools, we included the following sentence in the results section: “As shown in Fig. S1, Centrin-2 and POC5 proximity interactomes were enriched for GO categories that are relevant for their published functions during centrosomal, cytoplasmic and/or nuclear biological processes and related cellular compartments (Azimzadeh et al., 2009; Dantas et al., 2013; Heydeck et al., 2020; Khouj et al., 2019; Resendes et al., 2008; Salisbury et al., 2002; Steib et al., 2020; Yang et al., 2010; Ying et al., 2019).”

• We replaced the “interactome” statement with “proximity interaction maps” or “proximity interactors” throughout the manuscript to prevent the conclusion that the proximity maps represent the inner scaffold interactome. b) As the reviewer noted, most centrosome proteins have multiple different cellular pools including the centrosome. For most proteins like gamma-tubulin and centrin, their cytoplasmic/nucleoplasmic pools are more abundant than their centrosomal pools (Moudjou et al., 1996; Paoletti et al., 1996). For the Firat-Karalar et al. Current Biology 2015 paper, I compared the biotinylation levels of centrosomal fractions versus cytoplasmic fractions and confirmed that this is also true in cells expressing myc-BirA* fusions of CDK5RAP2, CEP192, CEP152 and CEP63 (unpublished) (Firat-Karalar et al., 2014). For the revised manuscript, we will compare the biotinylation level of centrosomal, nuclear and cytoplasmic pools of V5Bir*-POC5 and V5BirA*-Centrin-2 using the stable lines. To this end, we will use published centrosome purification protocols. We will include this data in Fig. S1 to highlight that the proximity interactomes represent the different pools of the bait proteins and to show the relative levels of the baits across their different pools.

c) BioID approach has been successfully used to probe centrosome interactions by my lab and other labs in the field. In fact, proximity interaction maps of over 50 centrosome proteins were published as resource papers by Pelletier&Gingras labs (Gheiratmand et al., 2019; Gupta et al., 2015). Analogous to our strategy in this manuscript, these studies generated proximity maps of centrosome proteins by creating cell lines that stably express BioID-fusions of centrosome proteins followed by streptavidin pulldowns from whole cell extracts and mass spectrometry analysis. Since majority of centrosome proteins also have pools in multiple cellular locations, the published BioID proximity maps for centrosome proteins are not specific to centrosomes. However, the proximity maps included all known centrosome proteins and identified new proteins, which shows that centrosome interactions are represented in pulldowns form whole cell lysates. Moreover, maps form whole cell lysates are also advantageous as they are are unbiased and can be used in future studies as resources for studying the functions and interactions of the bait proteins in different contexts.

In the Firat-Karalar et al. Current Biology 2015 paper, I combined centrosome purifications with BioID pulldowns to enrich for the centrosomal interactions in the proximity maps of centriole duplication proteins(Firat-Karalar et al., 2014). However, I started the purification with cells transiently transfected with the BioID-fusion constructs, which resulted in high ectopic expression of the fusions in the cytoplasm and/or nucleus. Therefore, centrosome enrichments were useful as an additional step before mass spectrometry. Comparative analysis of the data for proximity maps of 4 centrosome proteins generated from stable lines or centrosome fractions of transiently transfected cells substantially overlap as compared in the Gupta et al. Cell 2015 study and were more comprehensive (Table S2) (Gupta et al., 2015). Therefore, we are confident that the proximity interactomes we generated for POC5 and Centrin-2 include their centrosomal interactions.

__1b) Similarly, it is not clear whether the expression of Poc5 and Centrin-2 fusion molecules somehow interfere with their endogenous interactions or function. At least some loss-of-function (e.g., RNAi) experiments should be performed where the depletion of endogenous proteins should be attempted to rescue by the fusion constructs. This will help evaluate whether the fusion proteins can rescue the depletion of their endogenous counterparts and behave as expected from a wild-type scenario. __

The reviewer raises an important concern regarding the physiological relevance of the POC5 and Centrin-2 proximity maps. In the manuscript, we showed and discussed the validation of their proximity interactomes by two lines of evidence, which are: 1) the interactomes identified the previously described cellular compartments, biological processes or interactors of POC5 and Centrin-2, 2) the interactomes led to the identification of CCDC15 as a new inner scaffold protein.

As the reviewer indicated, stable expression of POC5 and Centrin-2 in the presence of their endogenous pools might affect cellular physiology and thereby the landscape of the interactomes. We plan to address this using the following experiments:

a) We will perform a set of functional assays to assess whether stable V5BirA*-Centrin-2 and V5BirA*-POC5 cells behaves like control cells in terms of their centrosome number, cell cycle profiles and mitotic progression. We will specifically quantify:

• centrosome number (immunofluorescence analysis for gamma-tubulin and centrin)
• their mitotic index (immunofluorescence analysis by DAPI)
• spindle polarity and percentage of multinucleation (immunofluoerescence analysis for microtubules, gamma-tubulin and DAPI)
• cell cycle profiles (flow cytometry and immunofluorescence)
• apoptosis (immunoblotting for caspase 3) Together, results from these experiments indicate that the V5BirA*-POC5 or Centrin-2-expressing stable lines do not exhibit defects associated with their stable expression.

b) We will perform expansion microscopy in V5BirA*-Centrin-2 and V5BirA*-POC5 cells to assess whether the fusion protein specifically localizes to the centriole inner scaffold, which will provide support for the presence of inner scaffold proteins in their proximity maps. Specifically, we plan to stain the fusion proteins by V5 or BirA antibodies and include the data for the antibody that works for expansion microscopy. This experiment will address whether their stable expression results in specific localization of these proteins at the centriole inner scaffold.

1c) Overall, as the entire claim around the proximity mapping revolve around its assumption about the centriole inner scaffold, these controls seem imperative to substantiate the ground truth of the biology presented in the manuscript.

In the revised manuscript, we toned down and made it clear that Centrin-2 and POC5 proximity maps are not specific to the inner scaffold and do not represent the inner scaffold interactome. Since the maps were generated from the whole cell extract, they will provide a resource for future studies aimed at studying functions and mechanisms of POC5 and Centrin-2 across their different cellular pools including the centrosome.

We would like to also highlight that the proximity maps of POC5 and Centrin-2 are not the major advances of our manuscript. The major advance of our manuscript is the identification of CCDC15 as a new inner scaffold protein that is required for regulation of centriole size and architectural integrity and thereby, for maintaining the ability of centrioles to template the assembly of functional cilia. Importantly, our results identified CCDC15 as the first dual regulator of centriolar recruitment of inner scaffold protein POC1B and the distal end SFI1/Centrin complex and provided important insight into how inner scaffold proteins work together during centriole integrity and size regulation. The new set of experiments we will perform for the revisions of the paper will strengthen these conclusions.

__2) I am curious about the choices of the cell lines in this work. The proximity mapping to reveal CCDC15 as a candidate protein for centriole inner scaffold was performed in HEK293T cells (human embryonic kidney), however its immunostaining was performed using RPE1 and U2OS cells (human retinal and osteosarcoma epithelial cells respectively). This raises questions regarding the generality of CCDC15 as a centriole inner scaffold protein. Could CCDC15 be simply unique to the centriole inner scaffold of epithelial cells such as RPE1 and U2OS cells? Or could the authors demonstrate any information/data on whether it's similarly localized to the inner scaffold in embryonic kidney cells or other cell types? If not, the claims should be moderated to reflect this fine detail. __

To test whether CCDC15 localizes to the inner scaffold in other cell types, we performed U-ExM analysis of CCDC15 localization relative to the centriolar microtubules in differentiating multiciliated epithelial cultures (MTEC). As shown in Fig. S3A, CCDC15 localized to the inner scaffold in the centrioles in MTEC ALI+4 cells. Given that the inner scaffold proteins including CCDC15 and previously characterized ones have not been studied in multiciliated epithelia, this result is important and provides support for potential role of the inner scaffold in ensuring centriole integrity during ciliary beating. Additionally, we examined CCDC15 localization by 3D-SIM in centrosomes purified from HEK293T cells, which showed that CCDC15 localizes between the distal centriole markers CEP164 and Centrin-3 and proximal centriole markers gamma-tubulin and rootletin (Fig. S3B).

3) Discussions and data on the localization of CCDC15 to centriolar satellites appear anecdotal and not fully convincing (Fig. S2D). Given that the authors test the relevance of PCM1 for CCDC15's centriolar localization, it is key to have quantitative data supporting their claim that centriolar satellites can help recruit CCDC15 to the centriole. Could the authors quantify what proportion of CCDC15 localize to the centriolar satellites? One way to do this could be to quantify the colocalization coefficience of CCDC15 and PCM1 signals.

We only observed co-localization of CCDC15 with the centriolar satellite marker PCM1 in cells transiently transfected with mNG-CCDC15. In Fig. S2E, we included the quantification of the percentage of U2OS and RPE1 cells that exhibit co-localization of PCM1 (100% of U2OS cells, about 80% of RPE1 cells). Like CCDC15, ectopic expression of WDR90 revealed its centriolar satellite localization, suggesting a potential link between centriolar satellites and inner scaffold proteins that can be investigated in future studies (Steib et al., 2020). We now included these results in the discussion section as follows:

“As assessed by co-localization with the centriolar satellite marker PCM1, mNG-CCDC15 localized to centriolar satellites in all U2OS cells and in about 80% of RPE1 cells (Fig. S2C-E). Association of CCDC15 with centriolar satellites is further supported by its identification in the centriolar satellite proteomes(Gheiratmand et al., 2019; Quarantotti et al., 2019).”

Even though endogenous staining for CCDC15 did not reveal its localization to centriolar satellites, following lines of data support the presence of a dynamic and low abundance pool of CCDC15 at the centriolar satellites: 1) CCDC15 was identified in the centriolar satellite proteome and interactome (Gheiratmand et al., 2019; Quarantotti et al., 2019). 2) CCDC15 centrosomal targeting is in part regulated by PCM1 (Fig. S2F, S2G). For majority of the proteins identified in the centriolar satellite proteome, their satellite pool can only be observed upon ectopic expression. This might be because their centriolar satellite pool is of low abundance and transient as satellite interactions are extensively identified only in proximity mapping studies, but not in traditional pulldowns

__4) Similar to above (#3), there is no quantitative information on the co-localization or partial co-localization of the signal foci in Fig. 3A and 3B. The authors readily study CCDC15's localization in wonderful detail in their expansion microscopy data, so they could actually consider taking out Fig. 3A and 3B, as the data seem redundant without any quantification. __

To address the reviewer’s concern, we included plot intensity profile analysis of CCDC15 and different centriole markers along a line drawn at the centrioles in Fig. 3A and 3B, which shows the extent of their overlap. As part of our revision plan, we will replace the confocal imaging data in Fig. 3A and 3B with 3D-SIM imaging data of CCDC15 relative to different centriole markers together with plot profile analysis. We already included 3D-SIM imaging of centrosomes purified form HEK293T cells in Fig. S3B. 3D-SIM imaging data will complement the localization data revealed by U-ExM.

__5) Do the authors also feel that CCDC15 localize to the core lumen in a somehow helical manner (Fig. 1A, Fig. 1F top and bottom panels, Fig. 5A etc.)? Le Guennec et al. 2020's helical lattice proposal for the inner scaffold further reaffirms that CCDC15 is indeed a likely major component of the inner scaffold. In my view, authors should state this physical similarity explicitly to further support their findings on CCDC15. __

As the reviewer indicated, cryo–electron tomography and subtomogram averaging of centrioles from four evolutionarily distant species showed that centriolar microtubules are bound together by a helical inner scaffold covering ~70% of the centriole length (Le Guennec et al., 2020). Although U-ExM data do not have enough resolution to show that CCDC15 localizes in a helical manner, we agree with the reviewer that the discussion of this possibility is important and thus we included the following sentence in the results:

“Longitudinal views suggest potential helical organization of CCDC15 at the inner scaffold, which is consistent with its reported periodic, helical structure (Le Guennec et al., 2020).”

__6a) The data on the link between the CCDC15 recruitment and the centriole growth (Fig. 4F) or the G2 phase of the cell cycle (Fig. 4H) are not fully convincing without quantitative data. For Fig. 4F, the authors should consider plotting the daughter centriole length vs the daughter CCDC15 intensities against each another, to see whether more elongated daughters truly tend to have more CCDC15. __

To address the reviewer’s concern, we will plot the daughter centriole length versus CCDC15 intensity at different stages of centriole duplication. In asynchronous cultures that we analyzed with U-ExM, we were not able to find enough cells to perform such quantification. To overcome this limitation, we will perform U-ExM analysis of cells fixed at different points after mitotic shake-off and stained for CCDC15 and tubulin. We will include minimum 10 different representative U-ExM data for different stages of centriole duplication in the revised manuscript along with quantification of length versus signal.

As detailed in the results section, the goal of these experiments was to determine when CCDC15 is recruited to the procentrioles during centriole duplication, but not to suggest a role for CCDC15 in centriole growth. We clarified this by including the following sentence:

“To investigate the timing of CCDC15 centriolar recruitment during centriole biogenesis, we examined CCDC15 localization relative to the length of procentrioles that represent cells at different stages of centriole duplication (Fig. 4F).”

__6b) For Fig. 4H, the argument regarding the cell cycle regulation requires quantification of the bands from several WB repeats, normalized to the expression of GAPDH within each blot (this is particularly relevant, as the bands of CCDC15 do not look dramatically different enough to draw conclusions by eye). __

We will perform these experiments two more times, quantify cellular abundance of CCDC15 in synchronized populations from three experimental replicates and plot it with proper statistical analysis.

__7a) The authors find herein that CCDC15 depletion lead to centrioles that are ~10% shorter than the controls. With the depletion of Poc5 and Wdr90 (other proposed components of the inner scaffold), the centrioles end up larger however (Steib et al., 2020). If the role of inner scaffold in promoting centriole elongation is structural, why are these two results the opposite of each other? I realize there is a brief discussion about this at the end of the paper, however, this requires a detailed discussion and speculation on the relevance of these findings. It would be key to clarify whether the inner scaffold as a structure inhibits or promotes centriole growth - or somehow both? If so, how? __

We agree with the reviewer that comparative analysis of centriole length phenotypes for CCDC15 and other components that regulate centriole length will provide insight into how these components work together at the centriole inner core. To this end, we phenotypically compared CCDC15 loss-of-function phenotypes to that of other components of the inner scaffold (POC5, POC1B, FAM161A) that interact with CCDC15. In agreement with their previously reported functions in U2OS or RPE1 cells, we found that POC5 depletion resulted in a 4% slight but significant increase in centriole length and POC1B depletion resulted in a 15% significant decrease. In contrast, FAM161A depletion did not alter centriole length (siControl: 447.8±59.7 nm, siFAM161A 436.3±64 nm). Together, our analysis of their centriolar localization dependency and regulatory roles during centriole length suggest that CCDC15 and POC1B might form a functional complex as positive regulators of centriole length. In contrast, POC5 functions as a negative regulator and might be part of a different pathway for centriole length regulation. We integrated the following sub-paragraph in the results section in pg. 19 and also included discussion of this data in the discussion section in pg. 23:

“Moreover, we quantified centriole length in control cells and cells depleted for POC5 or POC1B. While POC5 depletion resulted in longer centrioles, POC1B resulted in shorter centrioles (POC5: siControl: 414.1 nm±38.3, siPOC5: 432.7±44.8 nm, POC1B: siControl: 400.6±36.1 nm, siPOC1B: 341.5±44.39 nm,). FAMA161A depletion did not alter centriole length (siControl: 447.8±59.7 nm, siFAM161A 436.3±64 nm). Together, these results suggest that CCDC15 might cooperate with POC1B and compete with POC5 to establish and maintain proper centriole length.”

__7b) There might be some intriguing opposing regulatory action of Poc5 and CCDC15 as demonstrated here, where CCDC15 depletion leads to slightly over-recruitment of Poc5, and vice versa. Does this suggest that a tug-of-war going on between different molecules that localize to the inner scaffold? Does this provide some dynamicity to this structure, which might in turn regulate centriole length both positively and negatively? This may be analogous to how opposing forces of dyneins and kinesins provide robust length control for mitotic spindles. I am speculating here, but hopefully these may provide some useful grounds for further discussion in the paper. If the authors deem it interesting experimentally, they can test whether the two molecules indeed regulate centriole length by opposing each other's action, by a double siRNA of CCDC15 and Poc5 to see if this retains the centriole length at its control siRNA size (like how they do a similar test for Poc1's potential co-operativity with CCDC15 in Fig. 6J). __

We thank the reviewer for proposing excellent ideas on how inner scaffold proteins work together to regulate centriole length. As proposed by the reviewer, different proteins oppose each other analogous to how dynein and kinesin regulate mitotic spindle length. Loss-of-function and localization dependency data support that CCDC15 cooperates with POC1B, which was supported by phenotypic characterization of co-depleted cells (Fig. 6I-K).

The increase in POC5 levels and coverage at the centrioles upon CCDC15 depletion and vice versa (Fig. 7B, 7G) suggest that CCDC15 and POC5 compete with each other in centriole length regulation. As suggested by the reviewer, we attempted to test this by comparing centriole length in cells co-depleted for CCDC15 and POC5 relative to their individual depletions. Although we tried different depletion workflows, we were not able to co-deplete CCDC15 and POC5. Specifically, we tried transfecting cells with CCDC15 and POC5 siRNAs at the same time or sequentially for 48 h or 96 h. The centrioles in cells that survived co-depletion were positive for both CCDC15 and POC5. This might be because co-depletion of both proteins is toxic to cells. Since CCDC15 and POC5 are likely part of two different pathway in regulation of centrioles and also have other cellular functions, this might have caused cell death. We included the following statement in the discussion to address the excellent model proposed by the reviewer:

“Taken together, our results suggest that CCDC15 cooperates with POC1B and competes with POC5 during centriole length regulation. Moreover, they also raise the exciting possibility that centriole length can be regulated by opposing activities of inner scaffold proteins. Future studies that explore the relationship among centriole core proteins are required to uncover the precise mechanisms by which they regulate centriole integrity and size.”

__8) In their introduction section, the authors discuss how relatively little is known about the size control of centrioles, however they fail to mention a series of recent primary literature that uncover striking, new mechanisms and novel molecular players that highlight the complexity of centriole size control. This complexity appears to arise from the existence of multitude of length control mechanisms that influence the cartwheel or the microtubule length individually, or simultaneously via yet-to-be further explored crosstalk mechanisms. a. As such, when the authors talk about the procentriole size control in the introduction, they should discuss and refer to the following studies, in terms of: • How theoretical and experimental work demonstrate that procentriole length may vary dependent on the levels of its building block Sas-6 in animals (Dias Louro et al., 2021 PMID: 33970906; Grzonka and Bazzi, 2022 bioRxiv). • How a homeostatic Polo-like kinase 4 clock regulates centriole size during the cell cycle (Aydogan et al., 2018 JCB PMID: 29500190), and how biochemistry and genetics coupled with mathematical modelling unravel a conserved negative feedback loop between Cep152 and Plk4 that constitutes the oscillations of this clock in flies (Boese et al., 2018 PMID: 30256714; Aydogan et al., 2020 PMID: 32531200) and human cells (Takao et al., 2019 PMID: 31533936). __

__b. Similarly, when the authors refer to centriole size control induced by microtubule-related proteins, they should highlight the further complexity of this process by referring to: • How a molecule located at the microtubule wall, Cep295/Ana1, can regulate centriole length in flies (Saurya et al., 2016 PMID:27206860) and human cells (Chang et al., 2016 PMID:27185865) - like all the other centriolar MT molecules that the authors discuss in the manuscript. • How a crosstalk between Cep97 and Cep152 influences centriole growth in fly spermatids (Galletta et al., 2016 PMID:27185836). • How a crosstalk between CP110-Cep97 and Plk4 influences centriole growth in flies (Aydogan et al., 2022 PMID:35707992), and this molecular crosstalk is conserved, at least biochemically, in human cells (Lee et al., 2017 PMID:28562169). __

We thank the reviewer for highlighting the papers that uncovered new mechanisms and players of centriole size and integrity control as well as for the detailed explanation of how different studies led to these discoveries in different organisms. We should have discussed these proteins, functional complexes and mechanisms in our manuscript and cited the relevant literature. We inadvertently focused on literature that uncovered centriole length regulation by MAPs and the inner scaffold. In the introduction section of the revised manuscript where we introduced centriole size regulation in pg. 5, we summarized the major findings on the role of different MAPs, cartwheel and PLK4 homeostatic clock in ensuring formation of centrioles at the correct size in different organisms.

__Minor points: __

__1) Introduction section: Literature reference missing for the sentence starting with "Importantly, the stable nature of centrioles enables them to withstand...". __

We cited research articles that show the importance of centriole motility during ciliary motility and cell division.

“Importantly, the stable nature of centrioles enables them to withstand mechanical forces during cell division and upon ciliary and flagellar motility (Abal et al., 2005; Bayless et al., 2012; Meehl et al., 2016; Pearson et al., 2009).

__2) Fig. S1 legend: A typo as follows: CRAPome banalysis should read CRAPome analysis. __

We corrected this typo.

__3) Fig. S2: Info on the scale bar in the legend is missing in Fig. S2A. Scale bars for different panels are missing in general in Fig. S2A. __

We added scale bar information for Fig. S2A and to all other supplementary figure legends that lack scale bar information.

__4) Fig. 3A and 3B: When displaying the data, coloured cartoon diagrams would be beneficial to guide the reader who are not fully familiar with the spatial orientation of these proteins. __

As suggested by the reviewer, we will remove the confocal imaging data for CCDC15 localization from Fig. 3A and 3B. For the revised version, we will include 3D-SIM imaging data along with a diagram that represents the spatial orientation of CCDC15 relative to the chosen centriole markers.

__5) Fig. 3H: No information about the sample number (number of cells or technical repeats examined) reported. __

We included information on the number of experimental replicates and cells analyzed.

__6) Fig. S3B legend: A typo as follows: CCD15-depelted RPE1 cells should read CCDC15-depleted RPE1 cells. __

We corrected this typo.

__7) Fig. S3B legend: A typo as follows: cellswere fixed with should read cells were fixed with. __

We corrected this typo.

__8) There are many spelling mistakes and typos throughout the paper. I have listed a few examples above, but please carefully read through the manuscript to correct all the errors. __

Thank you for indicating the spelling mistakes we missed to correct for initial submission. In the revised manuscript, we carefully read through the manuscript to correct the mistakes.

__9) Fig. S3E: The orange columns depicting % of cells with Sas-6 dots look awkward. Why the columns look larger than the mean line? Please correct as appropriate. __

The total percentage of cells in the two categories (orange and purple) we counted is 100%, which corresponds to the column value at the y-axis. Therefore, the value for each experimental replicate for the orange category is less than 100% and is marked below the 100% line.

__10) Although authors provide microscopy information for the U-ExM and FRAP experiments, there is no information about the microscopy on regular confocal imaging experiments which should be detailed in Materials and Methods. Also, there is no information about the lenses, laser lines and the filter sets that were used in the imaging experiments. These should be provided as well. __

In the methods section, we now included detailed information for the microscopes we used and imaging setup (lenses, laser lines, filter sets, detectors, z-stack size, resolution).

11)

• __ Fig. 2A: lacks a scale bar. __
• __ Fig. 2C legend: lacks info on the scale bar length. __
• __ Fig. 5A legend: lacks info on the scale bar length. __
• __ Fig. 7A: lacks a scale bar. __
• __ Fig. 7G legend: lacks info on the scale bar length. __
• __ Fig. S2C-E: lack scale bars. __
• __ Fig. S3D, F and H: lack scale bars. (Fig. S4 in the revised manuscript)__
• __ Fig. S3J legend: lacks info on the scale bar length. (Fig. S4 in the revised manuscript)__
• __ Fig. S4A, B, D and E: lack scale bars. (Fig. S5 in the revised manuscript)__
• __ Fig. S4C legend: lacks info on the scale bar length. (Fig. S5 in the revised manuscript)__
• __ Fig. S4G legend: lacks info on the scale bar length. (Fig. S5 in the revised manuscript)__ We added the scale bars and the size information to the figures and figure legends for the above figures.

Reviewer #2 (Significance (Required)): __The findings of this study join among the relatively new literature (e.g., Steib et al., 2020 and Le Guennec et al. 2020) on the nature of centriole inner scaffold and its potential roles in centriole formation, integrity and its propensity to form the primary cilium. Therefore, it will be of interest to a group of scientists studying these topics in the field of centrosomes/cilia.

My expertise is on the biochemistry and genetics of centriole formation in animals.__

We thank the reviewer for his/her comments and constructive feedback to improve our manuscript. We are encouraged to see that the reviewer acknowledges how the results from our manuscript advances our understanding of centriole length, integrity and function regulation.

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I think recommendation algorithms are very interesting and complex because different social media platforms use different algorithms to showcase content for users. For example, when I use Instagram my recommended posts to view can be so different from my friends because we have different interests and interactions with the app. However, I do think these algorithms are become so accurate and complex it can be really creepy.

Author Response

Reviewer #1 (Public Review):

This is an interesting manuscript that proposes a new approach to for accounting for viral diversity within hosts in phylogenetic analyses of pathogens. Concretely, the authors consider sites for which a minor allele exist as an additional base in the substitution model. For example, if at a particular site 60% of reads have an C and 40% have a G, then this site is assigned Cg, as opposed to an C which is typical of analysing consensus sequences. Because we typically model sequence evolution as a Markovian process, as is the case here, the data become naturally more informative, given that there are more states in the Markov chain when adding these bases. As a result, phylogenetic trees estimated using these data are better resolved than those from consensus sequences. The branches of the trees are probably also longer, which is why temporal signal becomes more apparent.

I commend the authors on their rigorous simulation study and careful empirical data analyses. However, I strongly suggest they consider whether treating minor alleles as an additional base is biologically realistic and whether this may have implication for other analyses, particularly when there is very high within-host diversity and the number of states in becomes very large.

We thank the reviewer for the helpful and thorough review. We have included a paragraph in the Discussion regarding the biological interpretation of the 16-state model (Line 344-351), as well as the consequences when there’s high within-host diversity (Line 398).

Reviewer #2 (Public Review):

I agree that minor genetic variation could potentially be used to more accurately infer who-infected- whom in an outbreak scenario. Indeed, the use of minor genetic variation has proven very useful in reconstructing transmission chains for chronic infections such as HIV (e.g., see applications using Phyloscanner). To me, it seems that considering the full spectrum of viral genetic diversity within infected hosts would necessarily do the same if not better than considering only consensus-level viral sequence data. This is because there is a necessarily a loss of data and potentially a loss of information when going from considering the genetic composition of viral populations within a host to only considering the consensus sequences of those viral populations. As such, Ortiz et al.'s hypothesis stated on lines 66-70 is a reasonable one, and I was looking forward to seeing this hypothesis evaluated in detail in this manuscript.

R2.1 There are several parts of this manuscript I really like. In particular, encoding within-sample diversity as character states and using that alternative representation of sequence data for phylogenetic inference (as shown in Figure 3) is a very interesting idea, I think. There are some limitations that are not explicitly mentioned, however. For example, when using this 16-character state representation for phylogenetic inference, they assume independence between nucleotide sites. This is a major assumption that can be violated when considering longitudinal intrahost data and transmission dynamics in an outbreak setting, given genetic linkage between sites.

We have generated another set of simulations where the starting tree was a coalescent tree rather than a random phylogeny. This is described in the Results section, Line 228, and Figure 4—figure supplement 2. By using a coalescent tree, we increase the genetic linkage between sites. For all metrics used, the 16-state model performed better than the consensus sequence model. It is also important to note, as the reviewer points out, that longitudinal isolates should be removed from transmission inference, as we do in Figure 7 and Figure 7—figure supplement 2.. This point is now reflected in the Results (Line 286) and Methods (Line 534).

I have several major concerns about the work as it stands, particularly in the context of the SARS-CoV-2 application.

Concerns not related to the SARS-CoV-2 application:

R2.2 Figure 4 shows that a model using within-sample diversity can more accurately reconstruct evolutionary histories than a model that uses only consensus-level genetic data. This is really interesting. The Materials and Methods section (particularly lines 351-354) indicates that the sequence data were generated using certain specified substitution rates. The rates specified seem to be chosen in such a way to facilitate finding an improvement when using within-sample diversity. I don't know whether the relative rates of these 'substitutions' at all mirror "real-life". It would be very useful to have a broader set of analyses here to examine the effect of these 'substitution' rates on the utility of incorporating within-sample diversity into phylogenetic inference. (Also, 1, 100, 200 (line 353) inconsistent with 1, 20, 200 in Supp Table 3)

We have now corrected Supp Table 3 to reflect the rates described in the Methods section.

We defined our model with three rates: rate of minor variant acquisition, rate of minor-major variant switch, and rate of minor variant loss. We chose the rates for the simulations (1, 100, 200) to reflect a low rate of minor variant acquisition (1) and high rates of minor-major variant switch (200) and minor variant loss (100). These rates will result in pure bases (A,C,G and T) 100 times more likely to be present than low frequency variants, as seen in the base frequencies in Supp Table 1 and 3, which would in turn minimize the effect of including minor variations. We chose these rates to reflect the high turnover of minor variation often observed in real data and the frequencies of minor alleles in the SARS-CoV-2 dataset, but we agree with the reviewer that this may not always be the case. We also agree with the reviewer that changing the parameters in the simulations also affects the effect of including low frequency variation in the model. As such, we have now included simulations using different sets of rates (Figure 4—figure supplement ):

1) With a high rate of variant switch and loss compared to acquisition (1, 10, 100), reducing the frequency of minor variation.

2) With a lower rate of switch and loss (1, 10, 10), promoting a stable landscape of low frequency variation.

3) With no low frequency variation (Jukes-cantor model)

R2.3 Figure 5 is very interesting, particularly the results at bottleneck sizes of 1-10. What are the 'substitution' rates that are inferred here from using this simulated dataset? The Material and Methods section also does not mention the within-host viral generation time anywhere, as far as I can see (~line 384 states the mutation rate per base per generation cycle but not the length of the generation cycle anywhere).

Fastsimcoal2 is a coalescent simulator of population histories over several generations, given a population size and a mutation rate. For our purposes, transmissions are simulated as bottlenecks of constant size, and a generation is represented by each time step in the outbreak simulation, which corresponds to 1 day. This is further clarified in the Methods section (Line 475).

Concerns related to the SARS-CoV-2 application:

R2.4 I am very concerned about the testing of this hypothesis on the SARS-CoV-2 data presented. First, 1% is a very low variant calling threshold. Second, analysis of the 17 samples that were resequenced (out of 454) indicated that on average, 39% of iSNVS (intrahost single nucleotide variants) called between duplicate runs were only observed in one of the two runs (line 117). Their analysis in Figure 1 indicates that these discrepant (and seemingly spurious) variants occur at higher levels in high Ct samples (which makes sense; Figure 1b). They therefore decide to limit their analyses to samples with Ct values <= 30. This results in 249 samples. However, if we look at Figure 1b, only ~10% of iSNVs called across duplicate runs with Ct = 30 are shared! That means that 90% of iSNVs in the set appear to be spurious. If we assume that each duplicate run of a sample has approximately the same number of spurious iSNVs, then approximately 82% of iSNVs called in a sample with a Ct of 30 would be spurious. This fraction decreases with samples that have lower Ct values, but even at a Ct of 27, only ~60% of iSNVs called across duplicate runs are shared. All the downstream SARS-CoV-2 analyses based on within-host sample diversity therefore are based on samples where the large majority of considered sample diversity is not real. This leads to me necessarily discounting all of those downstream SARS-CoV-2 results.

We agree with the reviewer that, as the results show, datasets that incorporate within-sample low frequency variation are expected to have considerably more noise than using exclusively consensus sequences, and perhaps this wasn’t properly discussed in the manuscript. We have incorporated some notes about this in the Discussion section (Line 408-413).

The 1% variant frequency threshold was used to generate the analysis of Fig. 1 and Supp. Fig. 1-4. Looking at these results, we decided to establish the Ct cutt-off of 30 as mentioned by the reviewer, as well as a variant frequency threshold of 2% (as shown in the x-axis of Fig. 2). We overlooked this second variant frequency threshold in the manuscript, which has been added. As shown in Supp. Fig 4, this variant frequency threshold will increase the concordance between technical replicates, although some level of noise persists.

R2.5 Lines 153-167: I can't figure out how to square the quantitative results given in this paragraph with what is shown in Figure 2. To me, Figure 2 shows only that Technical Replicates have higher probabilities of sharing a variant than with 'No' relationship. What would also be helpful here so that the reader can get a better feel for the data would be to see the iSNV frequencies plotted over time for the longitudinal replicate samples in the supplement and, for the 'epidemiological' samples to show 'TV plots' in the supplement (as in Fig 3c in McCrone et al. eLife)

Figure 2 shows that technical replicates, longitudinal replicates, epidemiological samples and, in some instances, from the same department have a higher probability of sharing low frequency variants than those with no relationship (also shown in Supp Figure 5). However, also shown in Figure 2 is that the 95% CI is very wide, and therefore in many instances low frequency variants won’t be shared between epidemiological samples or samples from the same department.

We have also added Figure 2—figure supplement showing the low frequency variants plotted over time for longitudinal replicates. Unlike McCrone et al, we don’t have proven transmission between pairs of samples, although we believe our analysis also shows a pattern of shared low frequency variants among potential epidemiological links.

R2.6 Figure 6 and associated text: (a) root-to-tip distance: what units is this distance in? (b) That the authors find a temporal signal in these transmission clusters (where all consensus sequences within a cluster are the same) is interesting but also a bit baffling to me. Given the inference of very small transmission bottlenecks in previous studies (e.g., Martin & Koelle - reanalysis of Popa et al.; Lythgoe et al.; Braun et al.), I don't understand where the temporal signal comes in. Do the samples become more genetically diverse over the outbreak (this seems to be indicated in lines 260-262 but never shown and unlikely given bottleneck sizes)? Additional analyses to help the reader understand WHY within-sample diversity allows for the identification of temporal signal is important. This could involve plotting genetic diversity of the samples by collection date or some other, similar analyses.

a) The units of the y-axis (root-to-tip distance) are measured in substitutions per genome. This is now reflected in the legend of the figure.

b) As shown in Figure 5, even at small bottleneck sizes we are able to pick some of the diversity that evolves during the course of an outbreak. As hinted by the reviewer, the smaller the bottleneck the less diversity we can leverage for phylogenetic inference, and in fact for some epidemiological samples all the diversity will be lost during transmission, which is why many of the within-sample variants are not shared between the epidemiologically related samples. Figure 6 is indeed showing that the genetic distance (measured as number of substitutions per genome) increases per collection date. We have also added a Figure 6—figure supplement showing the increase in low frequency variants within outbreaks as the outbreaks progress in time (explained in Line 261 of the Results section), which explain in part the increasing temporal signal in clusters.

R2.7 Paragraph consisting of lines 229-238 and Figure 7: This analysis stops abruptly. What are the conclusions here? Figure 7a (right) seems inconsistent to me with Figure 7b and 7C results. Also, the main hypothesis put forward in this paper is that within-sample sequence data can better resolve who-infected-whom in an outbreak setting. Figure 7b and 7c however are never compared against analogous panels that use just consensus sequences. (Even though the consensus sequences are the same, according to Figure 7a, the inferences shown in Figures 7b and 7c could use additional data such as collection times, etc. that would provide information even when using exclusively consensus-level data). Also, do the analyses in Figures 7b and 7c use the 16-character state model at all? I think Supp Figure 9 is relevant here but not sure how?)

We have extended this section of the results to make it more coherent and clear (Line 284-293) and in the Discussion (Line 385-395). As added into the Discussion, we agree with the reviewer that even with equal sequences some inferences about transmission can be made with epidemiological data, specially collection dates. However, such data can’t be used to infer the genetic structure of the cluster, which complicates any analysis that can use a phylogenetic as input.

Additional concerns:

R2.8 Some of the stated conclusions, particularly in the Discussion section and in the Abstract, do not seem to be supported by the presented results. For example, line 27: 'within-sample diversity is stable among repeated serial samples from the same host': Figure 2 does not show this conclusively. Line 28: 'within-sample diversity... is transmitted between those cases with known epidemiological links': Figure 2 also does not show this conclusively. Line 29: 'within-sample diversity... improves phylogenetic inference and our understanding of who infected whom': Figure 7b/c results using within-sample diversity is never compared against results that use only consensus, so improvement not demonstrated. Line 272-273: 'samples with shorter distance in the consensus phylogeny were more likely to share low frequency variants'. Line 287: 'We demonstrated that phylogenies... were heavily biased'.

Line 27 and Line 28: We agree with the reviewer that the genomic analysis of SARS-CoV-2 sequences show only partial congruence within technical replicates and epidemiological links. We have appropriately addressed this in the Abstract.

Line 29 and Fig 7: Transmission inference using the consensus sequence in Figure 7b/c couldn’t be performed because the lack of any genetic difference between the consensus sequence meant that all sequences had the same transmission likelihood. This is now better explained in the Discussion section, lines 385-395.

Line 272-273: We have removed this section as we did not perform this analysis, as pointed out by the reviewer.

Line 287: The conclusion expressed in line 287 (now line 340) has been changed.

R2.9 The manuscript at times does not cite previous work that is highly relevant and thus overstates the novelty of the current work. For example: lines 21-23: '..conventional whole-genome sequencing phylogenetic approaches to reconstruct outbreaks exclusively use consensus sequences...' Phyloscanner uses within-sample diversity, for example, as does SCOTTI. These are finally cited in the discussion section (~line 310), but because this previous work is not acknowledged earlier in the manuscript, the novelty of the work presented here is somewhat overstated.

We have included background information in the introduction regarding the use of within-sample diversity for transmission inference (Line 69-73), as well as emphasizing that the novelty of our work lies more in the use of within-sample diversity in phylogenetic inference rather than exclusively transmission inference (Line 74, and other instance along the manuscript).

In sum, I think that the 16 character-state model is a very interesting model. More analyses on simulated data would be helpful to expand on when below-the-consensus level genetic data would truly be informative of phylogenetic relationships and who-infected-whom in outbreak settings. The SARS-CoV-2 analyses are very worrisome to me, given the inclusion of samples where the majority of considered within-sample genetic diversity is very likely not real. Some of the stated conclusions appear to either be at odds with the results presented or not directly evaluated.

Author Response

Reviewer #1 (Public Review):

In this interesting manuscript, Nasser et al explore long-term patterns of behavior and individuality in C. elegans following early-life nutritional stress. Using a rigorous, highly quantitative, high-throughput approach, they track patterns of motor behavior in many individual nematodes from L1 to young adulthood. Interestingly, they find that early-life food deprivation leads to decreased activity in young larvae and adults, but that activity between these times, during L2-L4, is largely unaffected. Further, they show that this "buffering" of stress requires dopamine signaling, as L2-L4 activity is significantly reduced by early-life starvation in cat-2 mutants. The paper also provides evidence that serotonin signaling has a role in modulating sensitivity to stress in L1 larvae and adults, but the size of these effects is modest. To evaluate patterns of individuality, the authors use principal components analysis to find that three temporal patterns of activity account for much of the variation in the data. While the paper refers to these as "individuality types," it may be more reasonable to think of these as "dimensions of individuality." Further, they provide evidence that stress may alter the strength and/or features of these dimensions. Though the circuit mechanisms underlying individuality and stress-induced changes in behavior remain unknown, this paper lays an important foundation for evaluating these questions. As the authors note, the behaviors studied here represent only a small fraction of the behavioral repertoire of this system. As such, the findings here are an interesting and very promising entry point for a deeper understanding of behavioral individuality, particularly because of the cellular/synaptic-level analysis that is possible in this system. This paper should be of interest to those studying C. elegans behavior and also more generally to those interested in behavioral plasticity and individuality.

We thank the reviewer for finding our results interesting.

Reviewer #2 (Public Review):

This paper set out to understand the impact of early life stress on the behavior and individuality of animals, and how that impact might be amplified or masked by neuromodulation. To do so, the authors built on a previously established assay (Stern et al 2017) to measure the roaming fraction and speed of individuals. This technique allowed the authors to assess the effects of early life starvation on behavior across the entire developmental trajectory of the individual. By combining this with strains with mutant neuromodulatory systems, this enabled the authors to produce a rich dataset ripe for analysis to analyze the complicated interactions between behavior, starvation intensity, developmental time, individuality, and neuromodulatory systems.

The richness of this dataset - 2 behavioral measures continuous across 5 developmental stages, 3 different neuromodulatory conditions (with the dopamine system subject to decomposition by receptor types) and 4 different levels of starvation, with ~50-500 individuals in each condition-underlies the strength of this paper. This dataset enabled the authors to convincingly demonstrate that starvation triggers a behavioral effect in L1 and adult animals that is largely masked in intermediate stages, and that this effect becomes larger with increased severity of starvation. Furthermore, they convincingly show that the masking of the effect of starvation in L2-L4 animals depends on dopaminergic systems. The richness of the dataset also allowed a careful analysis of individuality, though only neuromodulatory mutants convincingly manipulated individuality, recapitulating earlier research. Nonetheless, a few caveats exist on some of their findings and conclusions:

We thank the reviewer for the constructive comments. In the revised manuscript we include additional analyses and textual changes as detailed below, to address the points raised.

1) Lack of quantitative analysis for effects within developmental stages. In making the argument for buffered effects of starvation on behavior during periods of larval development, the authors make claims regarding the temporal structure of behavior within specific stages. However, no formal analysis is performed and and the traces are provided without confidence intervals, making it difficult to judge the significance of potential deviations between starvation conditions.

In the revised manuscript, we include additional analyses of roaming fraction effects across shorter developmental-windows, showing within-stage differences in behavioral patterns following starvation (Figure 1 - figure supplement 1E; Figure 3 - figure supplement 1C). In addition, we further temper and rewrite our conclusions to clearly describe these effects (now- “…while 1 day of early starvation modified within-stage temporal behavioral structures by shifting roaming activity peaks to later time-windows during the L2 and L3 stages…” in p. 4 and “Interestingly, during the L2 intermediate stage the effects on roaming activity patterns were more pronounced during earlier time-windows of the stage…” in p. 8).

2) Incorrect inferences from differences in significance demonstrating significant differences. The authors claim that there is an increase in PC1 inter-individual variation in tph-1 individuals, however the difference in significance is not evidence of a significant difference between conditions (see Nieuwenhuis et al. 2011). This undermines claims about an interaction of starvation, neuromodulators, and individuality.

In the revised manuscript we provide now a direct comparison of PCs inter-individual variances between starved and unstarved populations, demonstrating significant differences in inter-individual variation in specific PC individuality dimensions following stress (Figure 6 and Figure 6 - figure supplement 1). These results include the increase in PC1 inter-individual variation in tph-1 mutants following 3 and 4 days of starvation (Figure 6A,E).

3) Sensitivity of analysis to baseline effects and assumptions of additive/proportional effects. The neuromodulatory and stress conditions in this paper have a mixture of effects on baseline activity and differences from baseline. The authors normalize to the roaming fraction without starvation, making the reasonable assumption that the effect due to starvation is proportional to baseline, rather than an additive effect. This confound is most visible in the adult subpanel of figure 5d, where an ~2-3 fold difference in relative roaming due to starvation is clearly noted, however, this is from a baseline roaming fraction in tph-1 animals that are ~2 fold higher, suggesting that the effect could plausibly be comparable in absolute terms.

Unavoidably, any such assumptions on the expected interaction between multiple effects will be a gross simplification in complicated nonlinear systems, and the data are largely shown with sufficient clarity to allow the reader to make their own conclusions. However, some of the interpretations in the paper lean heavily on an assumption that the data support a direct interpretation (e.g. "neuronal mechanisms actively buffer behavioral alterations at specific development times") rather than an indirect interpretation (e.g. that serotonin reduces baseline roaming fraction which makes a fixed sized effect more noticeable). Parsing the differences requires either more detailed mechanistic study or careful characterization of the effect of different baselines on the sensitivity of behavior to perturbation-barring that it's worth noting that many of these interactions may be due to differences in biological and experimental sensitivity to change under different conditions, rather than a direct interaction of stress and neuromodulatory processes or evidence of differing neuromodulatory activity at different stages of development.

In the revised manuscript we added a discussion of the potential complicated interactions between neuromodulation and stress, altering baseline levels and deviations from baseline. We also discuss the interpretation of the results in the context of non-linear systems in which sensitivity of the behavioral response to underlying variations may be modified by specific neuromodulatory and environmental perturbations, without assuming direct differences in neuromodulatory states over development or across individuals (p. 16).

Reviewer #3 (Public Review):

In this study, Nasser et al. aim to understand how early-life experience affects 1) developmental behavior trajectory and 2) individuality. They use early life starvation and longitudinal recording of C. elegans locomotion across development as a model to address these questions. They focus on one specific behavioral response (roaming vs. dwelling) and demonstrate that early life (right after embryo hatching) starvation reduces roaming in the first larval (L1) and adult stages. However, roaming/dwelling behavior during mid-larval stages (L2 through L4) is buffered from early life starvation. Using dopamine and serotonin biosynthesis null mutant animals, they demonstrated that dopamine is important for the buffering/protection of behavioral responses to starvation in mid-larval stages, while in contrast, serotonin contributes to early-life starvation's effects on reduced roaming in the L1 and adult stages. While the technique and analysis approaches used are mostly solid and support many of the conclusions made in the manuscript for part 1), there are some technical limitations (e.g., whether the method has sufficient resolution to analyze the behaviors of younger animals) and confounding factors (e.g., size of the animal) that the authors do not yet sufficient address, and can affect interpretation of the results. Additionally, much of the study is descriptive and lacks deep mechanistic insight. Furthermore, the focus on a single behavioral parameter (dwelling vs. roaming) limits the broad applicability of the study's conclusions. Lastly, the manuscript does not provide clear presentation or analysis to address part 2), the question of how early life experience affect individuality.

We thank the reviewer for these important comments. As described below, in the revised manuscript we include new analyses (following extraction of size data), showing behavioral modifications across different conditions/genotypes also in size-matched individuals (within the same size range) (Figure 1 - figure supplement 1F; Figure 3 - figure supplement 1D,E; Figure 5 - figure supplement 1B,D). We also made edits to the text to describe these results (Methods p. 21 and Results section). In addition, while we can detect behavioral changes using our imaging method even in young L1 worms across conditions and genotypes (described in Stern et al. 2017 and this manuscript), as the reviewer correctly pointed out, we may miss some milder behavioral effects due to lower spatial imaging resolution in younger worms. We are now referring to this spatial resolution limitation in the revised manuscript (discussion part). Lastly, in the revised manuscript we added clearer and more direct analyses of changes in inter-individual variation in multiple PC dimensions following early stress, by directly comparing variation between starved and unstarved individuals within the mutant and wild-type populations (Figure 6; Figure 6 - figure supplement 1). These analyses show significant changes in inter-individual variation within specific PC individuality dimensions following early stress. Also, we made textual changes along the manuscript to increase the clarity of presentation of these results.

Author Response

Reviewer 1 (Public Review):

In this paper, Reato, Steinfeld et al. investigate a question that has long puzzled neuroscientists: what features of ongoing brain activity predict trial-to-trial variability in responding to the same sensory stimuli? They record spiking activity in the auditory cortex of head-fixed mice as the animals performed a tone frequency discrimination task. They then measure both overall activity and the synchronization between neurons, and link this ’baseline state’ (after removing slow drifts) of cortex to decision accuracy. They find that cortical state fluctuations only affect subsequent evoked responses and choice behavior after errors. This indicates that it’s important to take into account the behavioral context when examining the effects of neural state on behavior.

Strengths of this work are the clear and beautiful presentation of the figures, and the careful consideration of the temporal properties of behavioral and neural signals. Indeed, slowly drifting signals are tricky as many authors have recently addressed (e.g. Ashwood, Gupta, Harris). The authors are well aware of the difficulties in correlating different signals with temporal and cross-correlation (such as in their ’epoch hypothesis’). To disentangle such slow trends from more short-lived state fluctuations, they remove the impact of the past 10 trials and continue their analyses with so-called ’innovations’ (a term that is unusual, and may more simply be replaced with ’residuals’).

The terms ‘innovations’ and ‘residuals’ are sometimes used interchangeably. We used innovations because that’s how they were introduced in the signal processing literature (i.e., Kailath, T (1968). ”An innovations approach to least-squares estimation–Part I: Linear filtering in additive white noise.” IEEE transactions on automatic control). We try to be explicit in the text about the formal definition of this quantity, to avoid problems with terminology.

I do wonder if this throws out the baby with the bathwater. If the concern is statistical confound, the ’session permutation’ method (Harris) may be better suited. If the concern is that short-term state fluctuations are more behaviorally relevant (and obscured by slow drifts), then why are the results with raw signals in the supplement (Suppfig 8) so similar?

The concern was statistical confound, although this concern is ameliorated when using a mixed model approach and focusing on fixed effects. However, our approach allowed us to assess the relative importance of slow versus single-trial timescales in the predictive relationship between cortical state (and arousal) and behavior, revealing that, in the conditions of our experiment, only the fast timescales are relevant. Because of this, we think that the baby wasn’t thrown out with the bathwater as, qualitatively, no new phenomenology was revealed when the slow components of the signals were included. In hindsight, it is true that the results we obtained suggest that maybe the effort we made to isolate the fast component of the signals was unjustified. However, this can only be known after both options have been tried, as we did. Moreover, we started using innovations based on the results in Figure 2 where, as we show, the use of innovations does make a difference, even at the level of fixed effects in a mixed model. We agree that we could have used the ‘session permutation’ method, but given the depth at which we have explored this issue in the manuscript already, and the clarity of the results, we think that adding a third method would only make reading the manuscript more difficult without adding any substantially new content.

While the authors are correct that go-nogo tasks have drawbacks in dissociating sensitivity from response bias, they only cursorily review the literature on 2AFC tasks and cortical state. In particular, it would be good to discuss how the specific method - spikes, EEG (Waschke), widefield (Jacobs) and algorithm for quantifying synchronization may affect outcomes. How do these population-based measures of cortical state relate to those described extensively with slightly different signals, notably LFP or EEG in humans (e.g. work by Saskia Haegens, Niko Busch, reviewed in https://doi.org/10.1016/j.tics.2020.05.004)? This review also points out the importance of moving beyond simple measures of accuracy and using SDT, which would be an interesting improvement for this paper too.

We thank the reviewer for pointing us towards the oscillation-based brain-state literature in humans. We have expanded the paragraph in the discussion where we compare our results with previous work in order to (i) elaborate on the literature on 2AFC tasks, (ii) specifically address the literature linking alpha power in the pre-stimulus baseline and psychophysical performance, and (iii) mention different methods for assessing desynchronization. Our view is that absence of lowfrequency power is a robust measure which can be assessed using different types of signals (spikes, imaging, LFP, EEG). That said, the relationship between desynchronization and behavior appears subtle and variable, specially within discrimination paradigms. These issues are discussed in the paragraph starting in line 527 in the text.

Regarding the use of SDT, we had already established that our main finding could be expressed as a significant interaction between FR/Synch and the stimulus-strength regressor, when predicting choice after errors (Supplementary Fig. 4A in original manuscript), which is equivalent to a cortical state-dependent increase in d′ after the mice made a mistake. In order to consider a possible effect of cortical state on the ‘criterion’ (i.e., an effect on the bias of the mice towards either response spout), we re-run this GLMM but adding the cortical state regressors as main effects. The results show that the FR-Synch predictor is only significantly greater than zero as an interaction after errors (p = 0.0025). As a main effect, it’s not significantly different from zero neither after errors (p = 0.28), nor after correct trials (p = 0.97). We have included this analysis as Figure 3-figure supplement 1B (replacing the previous Supplementary Fig. 4A) and commented on them in the text (lines 222-225).

Reviewer 2 (Public Review):

The relationship between measures of brain state, behavioral state, and performance has long been speculated to be relatively simple - with arousal and engagement reflecting EEG desynchronization and improved performance associated with increases in engagement and attention. The present study demonstrates that the outcome of the previous trial, specifically a miss, allows these associations to be seen - while a correct response appears less likely to do so. This is an interesting advance in our understanding of the relationship between brain state, behavioral state, and performance.

This is probably just a typo, but we would like to clarify that the relevant outcome in the previous trial is not a miss, but an incorrect choice in an otherwise valid trial (i.e., a trial with a response within the allowed response window).

While the study is well done, the results are likely to be specific to their trial structure and states exhibited by the mice. To examine the full range of arousal states, it needs to be demonstrated that animals are varying between near-sleep (e.g. drowsiness) and high-alertness such as in rapid running. The fact that the trials occurred rapidly means that the physiological and neural variables associated with each trial will overlap with upcoming trials - it takes a mouse more than a few seconds to relax from a previous miss or hit, for example. Spreading the rapidity of the trials out would allow for a broader range of states to be examined, and perhaps less cross-talk between adjacent trials. The interpretation of the results, therefore, must be taken in light of the trial structure and the states exhibited by the mice.

We thank the reviewer for the positive assessment of our work and also for raising this point in particular. This motivated us to look more carefully at this issue, with results that, we believe, strengthen our study.

Author Response

Reviewer #1 (Public Review):

In this work, Roche et al. study a 13-year long time series of microbiome samples from wild baboons from Kenya. The data used in this work challenge a previous finding from the same authors that temporal dynamics in microbiome changes are largely individualized. Using a multinomial logistic-normal modeling approach, the authors detect that co-variance in temporal dynamics in microbial pair-wise associations among individuals occurs more frequently between relatives. Furthermore, the authors identify that microbial phylogenetic proximity is associated with consistent co-abundance changes over time and that their metric of universal microbial relationships is robust across hosts and is detected even in human longitudinal data. The authors conduct a thorough statistical revision of publicly available results, highlighting this time (e.g. compared to Björk et al, doi: 10.1038/s41559-022-01773-4) the consistently shared microbial properties between individuals, rather that the individual microbial signatures highlighted in their previous work.

Thank you for this summary. We would like to briefly clarify that we do not see the current work as inconsistent with our prior finding in Björk et al. that microbiome taxonomic compositions are idiosyncratic and asynchronized. However, this new analysis, which focuses on abundance correlations between pairs of taxa, indicates that the personalized compositions and dynamics we observed in Björk et al. are probably not attributable to personalized microbiome ecologies. In other words, Björk et al. showed that microbial taxa found in the guts of different baboons can be quite distinct (and remain so over time, giving rise to semi-stable individual signatures). The current study shows that, despite this taxonomic individuality, the correlations between pairs of microbes in the baboon gut are often quite consistent. To give a basic example, hot weather and ice cream, when observed, are often observed together (positively correlated), but while some places have a lot of both, some have little of either. This idea is discussed in more detail below (see response R6) and in the revised Discussion section (lines 572 to 586).

Strengths:

This work is foundational in its compelling effort to generate a rigorous method to evaluate coabundance dynamics in longitudinal microbiome data. The approach taken will likely inspire developments that will sharpen the capacity to extract co-varying microbial features, taking into account seasonality, diet, age, relatedness, and more. To the best of my understanding, their hierarchical model integrated into the Gaussian process to analyze microbial dynamics is reasonably robust and they clearly explain the implementation. Furthermore, this work introduces and defines the concept of a universality score for microbial taxon pairs. Overall, the work presented is clear and convincing and provides tools for the community to benefit from both methods and results. Furthermore, conceptually, this work stresses the value of consistent and shared microbial dynamics in groups, which enriches our understanding of host-associated microbial ecology, otherwise understood to be largely dependent on external fluctuations.

Weakness:

It is not entirely clear the extent to which the presented results revise, refute, or support the previously published analysis performed by the authors on the same dataset (doi: 10.1038/s41559-022-01773-4), which was more focused on individuality.

We agree the relationship between Björk et al. and the current manuscript was unclear in our original submission. We now elucidate the relationship between these papers in the Discussion (lines 572 to 586). Briefly, Björk et al. found that microbiome taxonomic compositions are idiosyncratic and asynchronized. The current analysis finds that pairwise bacterial abundance correlations are predominantly shared and not highly personalized. We think the most likely explanation is that, as mentioned by Reviewer 2 below, the current analyses do not account for the role that environmental gradients play in the gut. If these environments differ asynchronously across hosts, it could lead to shared abundance correlations, but individualized microbiome compositions and individualized single-taxon dynamics. We discuss this possibility and other potential explanations in the revised Discussion (lines 572 to 586).

Reviewer #2 (Public Review):

The authors of this paper identify a knowledge gap in our understanding of the generalizability of ecological associations of gut bacteria across hosts. Theoretically, it is possible that ecological associations between bacteria are consistent within a host organism but differ between hosts, or that they are universal across hosts and their environmental gradients. The authors utilize longitudinal data with a unique temporal resolution, on Amboseli baboons, 56 individuals who were sampled for gut microbiome hundreds of times over a decade. This data allows disentangling ecological dynamics within and across individuals in a way that as far as I know has never been done before. The authors show that ecological relationships among baboon gut bacteria, measure through a correlation based on covariation, are largely universal (similar within and across host individuals) and that the most universally covarying taxa are almost always positively associated with each other. They also compare these results with two sets of human data, finding similar patterns in one human data set but not in the other.

The main aim of this paper is to establish whether gut microbial ecologies are universal across hosts, and this the authors generally show to be true in a thorough and convincing way. However, some re-assessment or re-assurance on the solidity of their chosen method of estimating co-variation would be needed to fully assess the robustness of subsequent results. Specifically, the authors measure the correlation between microbial taxa from data on their abundance co-variation across samples. While necessary steps have been taken to validate the estimates across spurious correlations due to the compositional nature and autocorrelation structures present in the data, I worry that the sparsity of the data might influence the estimation of positive and negative correlations in a slightly different manner. There exist more microbial taxa than samples in the data and some taxa are present in as few as 20% of the samples, meaning that the covariation data will have a large amount of 0-0 pairs. I worry that the abundance of 0-0 pairs in the data might inflate the measures of positive co-variation, making taxa seem highly positively correlated in abundance when they in fact are missing from many samples. Of course, mutual absence is also a form of biologically meaningful covariation but taking the larger number of taxa than samples and the inability of sequencing technology to detect all low-abundance taxa in a sample, I am currently not convinced that all of the 0-0 pairs are modeled as a realistic and balanced way as a continuum of the other non-zero co-variation between taxa in the data. This may become problematic when positive and negative relationships are compared: The authors state that even though most associations between taxa were negative, the most universally correlated taxa pairs (taxa pairs with strongest correlations in abundance both within and between hosts) were enriched in positive associations. It may be possible that this is influenced by the fact that zero inflation in the data lends more weight to positive links than negative links. Whether these universal positive correlations are driven by positive non-zero abundance covariation or just 0-0 links in the data is currently unclear.

Thank you for pointing out this weakness in our original analyses. As described in response R1 above, your hunch was correct: zero inflation biased our correlation patterns such that taxa pairs with a high frequency of joint zero observations (i.e., where both members of the pair had very low or zero abundances) tended to be positively correlated (Fig. R1). Consequently, as you suggested, zero inflation in the data lent more weight to positive links than negative links in our data set. To address this problem in the revised manuscript, we now restrict our analyses to taxon pairs whose joint zero-abundance observations were less than 5% of all samples across hosts (pairs to the left of the dashed vertical line in Fig. R1 above). We also restricted our analyses to taxa observed in at least 50% of all samples. The first of these criteria was the most restrictive. As described above, our new filtering procedure retained 1,878 of the original 7,750 ASV-ASV pairs; 57 of the original 66 phylum-phylum pairs; and 473 of the original 666 class/order/family-level pairs.

Another additional result that would benefit from a more clear context is the result that taxa correlation patterns were more similar between phylogenetically close taxa and between genetically close host individuals. The former notion is to be expected if taxa abundances are driven by environmental (or host physiology-related) selective forces that favor bacteria with similar phenotypes. This yields more support to the idea that covariation is environmentally driven rather than driven by the ecological network of the bacteria themselves, and this could be more clearly emphasized. The latter notion of covariation being more similar in genetically related hosts is currently impossible to disentangle from the notion that covariation patterns were more similar with individuals harboring a more similar baseline microbiome composition since microbiome composition and genetic relatedness were apparently correlated. To understand if something about relatedness was actually influential over correlation pattern similarity, one would need to model that effect on top of the baseline similarity effect. Currently, it is not clear if this was done or not.

We agree that shared responses to environmental gradients within hosts—especially immune profiles and pH—could explain both of these findings. These ideas are now described in the Discussion in lines 559 to 562.

We also now report partial Mantel tests to control for baseline similarity in microbiome composition when testing for shared microbial correlation patterns among genetic relatives. Controlling for baseline similarity had little effect on the results, and we now report the statistics for this partial Mantel (Fig. 5B; Table S7; r2=0.009; partial Mantel p-value=0.002). See lines 391-392.

The authors also slightly overemphasize the generalizability of their results to humans, taking that only one of the human data sets they compare their results to, shows similar patterns. While they mention that the other human data set (that was not similar in patterns to theirs) was different in some key aspects (sampling frequency was much higher), the other human data set was also dissimilar to the other two (it only contained infants, not adults). Furthermore, to back up the statement that higher sampling frequency would be the reason this data set had dissimilar covariation between taxa, one would need to show that the temporal variation in this data set was different from the baboon one and show that these covariation patterns were sensitive to timescale by subsampling either data to create mock data sets with different sampling frequency and see how this would change the inference of ecological associations.

We have revised the text to tone down the generalizability of our results to humans. For instance, the abstract (line 58) now states that “universality in baboons was similar to that in human infants, and stronger than one data set from human adults” but does not state that our results are generalizable to humans.

We also considered sub-sampling the data set from Johnson et al., from daily to monthly scales, but unfortunately that data set is only 17 days long, so doing so is impossible. This is now stated in the Discussion in line 619, which states, “However, without the ability to subsample Johnson et al. [7] to monthly scales (this data set is only 17 days long), it is impossible to test this prediction.”

To the extent that the results are robust, particularly regarding to the main result of the universality of gut microbial ecological associations, the impact of this paper is not small. This question has never been so thoroughly and convincingly addressed, and the results as they stand have the power to strongly influence the expectations of gut microbial ecology across many different systems. Moreover, as the authors point out, evidence for universal gut microbial ecology is important for the future development of probiotics. An important point here, underemphasized by the authors, is that universal gut microbe ecologies will allow specific interventions that use gut microbe ecology to manipulate emergent community properties of microbiomes to be more beneficial for the host, rather than just designing compositional cocktails that should fit all. In addition to the main finding of this study, the unique data set and the methods developed as part of this study (e.g. the universality score, the enrichment measures, the model of log-ratio dynamics, the assessment of covariation from time-ordered abundance trajectories) will doubtlessly be translatable to many other studies in the future.

Thank you for these suggestions. We now mention these implications in the introduction (line 82-84) and in the discussion in lines 537-539 and line 630.

Reviewer #3 (Public Review):

This is a well-executed study, offering thorough analysis and insightful interpretations. It is wellwritten, and I find the conclusions interesting, important, and well-supported.

Thank you for your supportive comments.

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Reviewer 3: Wyeth Wasserman

SYNOPSIS The manuscript describes an updated release of the ReMM regulatory variant mutation scoring system. The paper presents the performance of an updated version of the system and describes how it was applied to the most current release of the reference human genome.

OVERALL PERSPECTIVE This is a valuable resource for the community of researchers and clinicians working on the interpretation of genetic variants in the human genome. The work appears to be thoughtfully done and appropriate assessments have been provided. The use of the random forest models to weigh the contributions of features was particularly noted for the insights it provided into how features contribute to prediction. My biggest concerns are stylistic, which falls outside the scientific quality of the work. I provide these comments for the authors to consider and do not expect that my stylistic preferences will be uniformly accepted. A fair amount of justification of the manuscript focuses on the value of having a release for version 38 of the human genome, pointing to the field as not having done so broadly. I think this is misguided, as by the time people are reading the manuscript such points will have lost relevance. I suggest a focus on the science be given, as there is no need to justify things based on where other resources have progressed in releasing their version 38 updates. Points below include language/text clarifications that can be assessed by the authors. Writing styles differ, so stylistic comments should be optional.

MAJOR POINTS None. Well done and clearly presented.

MINOR POINTS 1. The word "various" is vague and often shows up when people are too busy to provide an accurate statement. Starting the manuscript with it makes a bad impression on this reader. You do not have to change it, but I thought you might appreciate knowing this impression. You could delete it with no harm to the sentence. (Not to get carried away, but the next sentence starting with "some" heightens the impression of 'hand waving'.) 2. I think I understand ", we apply cytogenic band-aware cross-validation using ten folds" but I encourage the authors to provide clearer wording for this point. 3. I would allow the reader to make their own judgement of performance. So please remove "excellent" from "we achieve an excellent performance" 4. "Rather than using ReMM scores for ranking, some users need to specify score thresholds" is confusing. I would change 'need to' to 'choose to' 5. "with lots of false positives" is a bit informal. I suggest "with a high false positive rate" 6. I am confused by "from three genomic regions (genic content and not overlapping with assembly gap changes) " as the brackets include two items, not three. 7. "maybe due to better mapping" - "maybe" should be "may be" 8. I think the language like "seems to be the only tool directly trained on training data and features derived from GRCh38." Is not particularly valuable long term. This is a useful contribution, but many tools are being updated to 38 and by the time this appears and is read, such statements decline in relevance. I would focus on providing this valuable resource, and not try to justify it based on a transient perception of where the field stands in updating versions. 9. "It is worth noting that in the context of extremely unbalanced data…" - you do note it. So I would change the wording to "In the context of extremely unbalanced data…"

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

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Reply to the reviewers

Detailed Answer to the Reviewers

Reviewer #1

__Summary __

The authors used a novel imaging technique to monitor glutamate release and correlated these measurements with gold standard electrophysiological measurements. The genetically encoded glutamate reporter, iGluSnFR, was expressed in mouse spiral ganglion neurons using the approach described in Ozcete and Moser (2021, EMBO J). The iGluSnFR signals and the postsynaptic currents were measured at the endbulb of Held synapse. A small effect of the expression of iGluSnFR on the mEPSC kinetics was found (but see comment 1). Furthermore, deconvolution of the iGluSnFR signals was performed enabling the comparison of some presynaptic properties assessed with either iGluSnFR or electrophysiology.

We thank the reviewer for her/his appreciation of our work and for the comments that have helped/will help us further improve our manuscript.

__Major comments __

1. The central finding of the study is the prolonged decay time constant of the mEPSC. The difference is small but astonishingly significant (0.172 {plus minus} 0.002 and 0.158 {plus minus} 0.001, P=0.003). The SEM is about 100 times smaller than the measured time constant. This is biologically not plausible. Therefore, I am skeptical about the statistical significance of the results.

We appreciate the feedback of the reviewer. We agree that our presentation of the data was easy to misunderstand and we changed it (see below). We modeled the statistical relationship of kinetic parameters with a mixed effects model (as described in methods). Since the presentation of regression parameters for this kind of data is not very usual in synaptic neuroscience (nor very informative in this study), we instead opted to report SEM and a p-value derived from the fit of the linear mixed effects model. For the SEM, there is no clear way to take into account the clustered nature of the data, so we calculated the SEM over all observations. Since the SEM is proportional to 1/sqrt(n) and the number of recorded mEPSCs is very large, this does indeed yield a very small SEM. We agree that reporting the SEM over all observations is unusual and leads to misunderstandings in this case. Now, we instead report the re-calculated the mean / SEM for all parameters over the median values per cell. We changed the presentation of the data also for the other values presented in the MS in all tables and the relevant parts of the main texts.. We note that the summary statistics do not directly influence the further statistical modeling.

1. Analysis of the size of RRP with electrophysiology and iGluSnFR is potentially interesting but iGluSnFR recordings could not resolve the spontaneous fusion of single vesicles. Therefore, it is not possible to estimate RRP with these iGluSnFR recordings. This limitation of the approach should be emphasised more clearly.

Yes, we think the inability to resolve single vesicles is one of the major limitations of the study and we note this in the introduction and in the relevant section of the discussion. We agree that it should be clear in the relevant section that we are not able to measure RRP size without resolving single vesicle release and modified the wording of the relevant results section to reflect this better (line 267, 497). We still believe that the cumulative release analysis is potentially interesting to researchers in the field, as RRP size is not the only parameter that can be estimated in this way. In particular, an estimation of the release probability in resting conditions is possible by dividing the amplitude of the first response (i.e. response to a single stimulus) by the RRP estimate even without knowing the exact number of vesicles that comprise either.

1. The control conditions (no surgery/no virus injection) are not the correct conditions for comparison with the experimental conditions (surgery/virus injection and sensor expression). The control group should be operated and injected with saline or ideally with a virus expressing GFP at the extracellular membrane. The authors addressed this issue by citing their previous work (Özcete and Moser, 2021). However, I am not convinced that surgery does not induce subtle changes that could explain the small differences in mEPSCs.

This is an excellent point that should be addressed in further research. A slowed decay would be consistent with the idea that iGluSnFR affects glutamatergic transmission by buffering glutamate, but we cannot rule out subtle changes due to the postnatal surgery or AAV-mediated transgene expression. In response to the reviewer’s comment, we modified the text to reflect the possibility of surgery and / or other parts of the expression system being responsible for the changes. We also discuss further control experiments (line 408). Finally, we believe that our comparison is still relevant for researchers using iGluSnFR in the system, as they will be asking if introducing a measurement system affects the underlying quantity.

__Minor comments __

The supplementary figures are not listed in the order in which they appear in the main text.

We now list the supplementary figures in the order in which they appear in the main text.

Figure 2B and 3 are not referenced in the main text.

We now reference the figures in the text.

The PPR in Figure 3 shows a PPR that cannot be evaluated because of the unusual plot with lines that are too thick.

We updated Fig.3 and chose a more straight forward way to display the PPRs.

Line 105: "...while simultaneously monitoring currents in postsynaptic cells". This sentence is not correct given that the EPSCs have not been shown yet at this point of the manuscript.

We removed this part of the sentence.

Line 110: "SV and are not cause are cause by spontaneous action potentials...". The sentence does not make sense.

We corrected the sentence.

Line 168-9: "...we did not find significant differences in amplitude and kinetics...". According to Table 2 (2mM Ca2+ condition), both Imax and Q appear to be almost twice as high in iGluSnFR as in control (2.05 {plus minus} 0.06 and 1.34 {plus minus} 0.03, respectively; P=0.241). Is this not a significant difference?

The difference was not significant. The misunderstanding likely stems from the same problem in the presentation of the values as for the mEPSCs. We replaced the SEMs with the SEMs of the cell median to avert this.

Table 4. 2mM Ca2+ condition. The Rrefill parameter is about an order of magnitude smaller in the iGluSnFR-expressing group. Is this correct or just a typo?

Thank you for spotting this: it was an error with regards to unit conversion. The value for the control group was off by a factor of 10. We corrected this mistake.

Referees cross-commenting

I also agree with the comments of the other reviewers.

Significance

General assessment

This topic is currently of interest because iGluSnFR techniques are widely used. However, the study is preliminary. The scientific progress in terms of quantity and quality is limited. For example, Figs. 1 and 5 show only images and traces with little scientific significance.

Advance

The main advance of the study is the implementation of the deconvolution of the iGluSnFR signal and the comparison of the back extrapolation with the first stimulus (Fig. 6). This comparison was similar between electrophysiology and iGluSnFR when deconvolution of the iGluSnFR data was performed. These data therefore argue against saturation of iGluSnFR, as expected from a large number of previous analyses of iGluSnFR.

There is little methodological improvements compared with the group's previous study (Ozcete and Moser, 2021 EMBO J). In this earlier study, a different synapse was analyzed but the same iGluSnFR was injected into the scala tympani of the right ear through the round window in the same way as in this study. Surprisingly, the authors do not refer to Ozcete and Moser (2021) in the relevant methods section.

Thank you for spotting this omission. We now cite Özçete and Moser (2021) in the appropriate place in the methods section as well.

Reviewer #2

Summary

In the manuscript 'Optical measurement of glutamate release robustly reports short-term plasticity at a fast central synapse' the authors present a careful analysis of whether direct measurements of transmitter release using the genetically-encoded indicator iGluSnFR, are suitable for assessing changes in transmitter release at the spiral ganglion neuron end bulbs of Held in the mouse cochlear nucleus. What sets this study apart from other studies, which have demonstrated the utility of iGluSnFR measurements, is the use of a camera-based fluorescence readout as opposed to confocal or 2P microscopy methods and that it is performed in the cochlear nucleus.

The primary methodology is the comparison of electrophysiological measurements of excitatory postsynaptic currents from bushy cells with fluorescence changes in the end bulbs of iGluSnFR expressing auditory nerve fibers with and without stimulation of the auditory nerve fibers. The experiments are technically demanding and introducing genetically encoded indicators in neurons of the cochlea is no small accomplishment. An important observation is that mEPSCs are slightly modified (prolonged) due to expression of iGluSnFR in the presynaptic end bulbs. This is perhaps not surprising as iGluSnFR binds glutamate and may act as a buffer to reduce the peak and slightly prolong the increase in cleft glutamate concentration after release from synaptic vesicles. To my knowledge, others have not reported iGluSnFR effects on mEPSCs. Perhaps earlier studies have not checked as carefully, alternatively previous studies had a too-low fraction of presynaptic terminals expressing iGluSnFR (or less expression of iGluSnFR) to detect a change in EPSC parameters, or this is a synapse-specific phenomenon. However, the authors demonstrate that EPSCs evoked by electrical stimulation of the auditory nerve fibers are unaffected by expression of iGluSnFR in the presynaptic neurons. Further findings are that the determined decay time constant is substantially longer than at other synapses (~16 ms at hippocampal synapses, Dürst et al., 2018). Synaptic depression was robustly reported by iGluSnFR at this synapse, but determination of single quantal events and thus quantal analysis was not really possible at this synapse using iGluSnFR in conjunction with the imaging and analysis techniques presented. The manuscript is carefully written and presented.

We thank the reviewer for her/his appreciation of our work and for the comments that have helped/will help us further improve our manuscript.

Major points

1) The ROIs are selected to be 'outer bounds' of the glutamate spread from the synapses being studied. My concern is that these generously-sized ROIs include signal from many iGluSnFR molecules which are distal to the release sites and thus will be reached only slowly by low concentrations of glutamate or be contributing only noise and no changes in fluorescence. I suggest the temporal resolution could be improved by restricting the analysis of fluorescence changes to fewer pixels within the ROIs with the fastest rising/highest amplitude responses.

Thanks for this helpful comment: The data in our data set should be well-suited to perform this analysis in addition to the presented analysis and so we added this new analysis to the Revision Plan.

2) The observation that despite a 2 fold increase in eEPSCs when changing from 2 mM to 4 mM extracellular calcium there is no change in iGluSnFR peak is curious as pointed out by the authors but not really discussed.

We don’t currently have an obvious explanation but consider saturation of the iGluSnFR peak response likely to contribute. In response to the comment of the reviewer, we have added the analysis of integrated iGluSnFR data, which we previously found to be more robust toward saturation than the peak, to the revision plan. We plan to add the relevant discussion along with the new analysis.

Are the traces presented in Figure 5 examples from the same recording?

Traces in fig. 5 are grand averages (wording modified for clarity). Unfortunately, it was not possible to routinely measure iGluSnFR responses from the same cell in 2mM Ca2+ and 4 mM Ca2+ as the time needed for the protocols was rather long which influenced cell stability and imaging conditions would deteriorate during the exchange of the bath solution. We think it is not quite possible to directly compare the absolute iGluSnFR responses at different extracellular Ca2+ levels.

Assuming the examples are from one cell I first assumed the lack of change of peak was saturation of iGluSnFR but the larger fluorescence change with 100 Hz stimulation suggests otherwise. How many endbulbs are contacting one BC? Do you capture iGluSnFR responses from only one or several? In the previous point I suggested that restricting analysis to the soonest reacting pixels might improve temporal resolution but in the case of detecting the peaks with higher and normal calcium, these fastest reacting signals are probably also more likely to be saturated with glutamate.

The eEPSCs elicited by this stimulation paradigm are monosynaptic (see methods / electrophysiology section), but there might be other iGluSnFR expressing endbulbs on the same bushy cell. Since we reduce the current just enough such that any further reduction leads to a complete failure to elicit an EPSC, we believe these additional endbulbs are not releasing glutamate. We cannot, however, exclude the possibility that iGluSnFR on neighboring structures captures any potential spillover glutamate.

Minor points

• mEPSCs are usually recorded in tetrodotoxin, I didn't find any mention in methods/results

In this system, sEPSCs are not affected by TTX (Oleskevich and Walmsley, 2002) and thus usually recorded without adding TTX. We discuss this more explicitly and added a clarification to reflect this assumption (on line 111).

• the large numbers of abbreviations make it difficult in places to follow the manuscript please at least define them again in the figure legends (e.g. BC, AVCN in figure 1, Q, FWHM in figure 2 etc.)

We went over the manuscript again and removed some abbreviations or redefined them in captions.

• it is a bit unusual to report results of a Wilcoxon test and at the same time mean and SEM instead of medians, if different tests were used then it is important to indicate this where the p values are given or make the sentence in the methods more definitive

We agree that the initial presentation of the data was ambiguous. We changed the presentation to reflect this (see also answer to reviewer 1).

• the liquid junction potential is reported as 12 mV, pretty sure it should be -12 mV (unless the QX-314 or some other of the more exotic ingredients in the extracellular solution is having a dramatic effect on the LJP).

We follow the usual conventions of P. H. Barry, Methods in Enzymology, Vol. 171, p. 678, as described in E. Neher, Methods in Enzymology, Vol. 207, p. 123, in which the LJP is defined as the potential of the bath solution with respect to the pipette solution. We subtracted this positive potential (+12mV) in the end to obtain the membrane potential which therefore was more hyperpolarized than the nominal potential.

I wonder if one of the faster/lower affinity iGluSnFR variants would be better suited for studying this synapse.

We agree with the reviewer that future studies should explore the potential of faster/lower affinity iGluSnFR variants for studying the endbulb synapse. The reasons why we employed the original version include: i) sharing the same mice for studies of cochlear ribbon synapses (Özcete & Moser, 2021) and cochlear nucleus synapses (this MS) for the sake of reducing animal experiments, ii) good signal to background facilitating our first study establishing the recording in brainstem slice, iii) less signal to background and shorter signals with the new variants (as found in preliminary recordings from cochlear ribbon synapses) that would make the endbulb recordings more challenging. We have added the following statement to discussion. “Future imaging studies of glutamate release at calyceal synapses should explore the potential of new iGluSnFR variants with lower affinity that provide more rapid signal decay. This will ideally go along with imaging at higher framerate and might require stronger intensities of the excitation light to boost the fluorescence signal.” on line 430.

The paper would benefit from a careful reading to shorten the text and to check for clarity. For instance page 15 line 436 I don't understand how 'the results can reduce the likelihood of biologically relevant changes'. I think the authors meant something different

Thank you for spotting this. We reworded the sentence (now on line 399): "The data on hand suggests that this is not the case. Firstly, even if a larger sample size may uncover more subtle effects neurotransmission of evoked events, our measurements suggest a small effect size. Secondly, even as we did find changes in mEPSC, it is probable that the biological significance is limited"

• page 5 'width' is misspelled

Fixed.

• page 18 'strychnine' is misspelled

Fixed.

• on many of the figures is text that it much too small

We went through the manuscript and increased the text size in the figures, where appropriate.

__Referees cross-commenting __

I agree with all the comments of the other reviewers - both raise the point that there should be a 'control' AAV injected for comparison of the mEPSCs which I missed but is of course quite important. See https://pubmed.ncbi.nlm.nih.gov/24872574/ for a study of AAV serotype-dependent effects on presynaptic release.

We now added a section on other possible factors influencing the results, citing the study above.

Significance

The main audience for this paper will be fairly specialized. Researchers interested in properties of presynaptic release and some specialists in synaptic transmission in the auditory system will be the main readers/citers of this work.

The work is an important technical/methodological report. It highlights an important effect of expressing iGluSnFR and also demonstrates that the effect is overall not very problematic. Additional problems using iGluSnFR are also indicated.

I am an electrophysiologist, studying synaptic transmission and plasticity with experience using a wide range of optogenetic tools

Reviewer #3

__Summary __

In the present manuscript, the authors explore the information that can be obtained using optical measurement of glutamate release with iGluSnFR on synaptic dynamics in the endbulb of Held.

They virally express iGluSnFR in presynaptic terminals, patch the postsynaptic cells and combine high-frame-rate optical recordings with electrophysiological measurements. Their first finding is that mEPCSs are prolonged when presynaptic cells express the glutamate indicator, which they interpret as buffering of extracellular glutamate by the indicator. Next, they repeated the experiment, this time with stimulating evoked EPSCs. In contrast to the previously observed effects, iGluSnFR did not affect the time course or the amplitude of the evoked EPSCs. The authors then asked whether iGluSnFR signals can be used to study synaptic dynamics, specifically, synaptic depression. In these experiments, the authors observed a change in the paired-pulse ratio with ISI of 10ms, but not longer intervals. They analyzed presynaptic release and did not find statistically significant differences.

Can iGluSnFR signals be used for the analysis of synaptic release? When stimulated at a low frequency of 10Hz (allowing the fluorescence to return close to baseline levels in between pulses), iGluSnFR dynamics were somewhat comparable to postsynaptic signals. At higher frequencies, the slow time course of the indicator prevented the identification of individual responses and the resulting fluorescence had a very different shape. To resolve this problem, the authors used deconvolution analysis (fig 6). This analysis revealed a linear relationship between the optical readout and the patch-clamp data.

I find the manuscript to be clearly written, the findings are well presented and discussed and are novel and of substantial interest to neuroscientists in the field. I do have a number of questions about experiments and analysis that may have an effect on the conclusions of this work.

We thank the reviewer for her/his appreciation of our work and for the comments that have helped/will help us further improve our manuscript.

1. In experiments comparing the effects of iGluSnFR expression on release dynamics (figure 1-4), the authors compare infected presynaptic cells to control (uninfected). The assumption is that synaptic buffering by iGluSnFR may affect glutamate diffusion in the synaptic cleft. However, it is possible that viral infection itself changes presynaptic properties. The authors should compare release from cells infected with GFP or a comparable indicator.

We agree that this is an important control experiment to be done in the future and that causal attribution is not in the scope of this study. A slowed decay would be consistent with the idea that iGluSnFR affects glutamatergic transmission by buffering glutamate, but we cannot rule out subtle changes due to the postnatal surgery or AAV-mediated transgene expression. In response to the reviewer’s comment, we modified the text to reflect the possibility of surgery and / or other parts of the expression system being responsible for the changes. We now also discuss further control experiments (line 408). Finally, we believe that our comparison is still relevant for researchers using iGluSnFR in the system, as they will be asking if introducing a measurement system affects the underlying quantity.

1. Analysis of pool parameters presented in table 4 indicates almost doubling of RRP size with iGLuSnFR with 2 mM Ca++. While not significant, this result may indicate a real effect that may have been missed due to low power (N=3 and 7 for these experiments). I do not believe the authors did a power analysis in this study. How was the number of experiments determined? I would suggest increasing the number of experiments to avoid type II errors.

We thank the reviewer for this critical comment. Indeed, we would also have liked to have a greater statistical power for these experiments, but had to face the situation that the establishing the method required more animals than expected and the animal license did not offer further animals for the analysis. Moreover, we note that the obtained RRP size estimates were generally lower compared to previous estimates of our lab for the endbulb synapse (e.g. Butola et al., 2021: ~20 nA for 2 mM Ca2+ in Fig. 5). This can partially be attributed to the use of cyclothiazide in previous studies, which we avoided given reports of presynaptic effects of cyclothiazide. As the series resistances of the included recordings were below 8 MOhm (mean series resistances: 2mM Ca, injected: 5.58 MOhm; 2mM Ca, control: 5.93 MOhm; 4mM Ca, injected: 5.75 MOhm; 4mM Ca, control: 6.0 MOhm) and series resistance compensation was set to 80% we do not expect clamp-quality to contribute to the smaller estimates in the present data set.

We have now added a statement noting the preliminary nature of these results and indicated that further experiments will be required to more certainly conclude on potential effects of iGluSnFR or the manipulation on endbulb transmission: “Our preliminary train stimulation analysis of vesicle pool dynamics in the presence and absence of AAV-mediated iGluSnFR expression in SGNs has not revealed significant differences between the two conditions. Further experiments, potentially involving faster versions of iGluSnFR and employing trains of different stimulation rates for model based analysis of vesicle pool dynamics (Neher and Taschenberger, 2021) will help to assess the value and impact of iGluSnFR in the analysis of transmission at calyceal synapses.” on line 381.

1. The deconvolution analysis assumes an instantaneous rise time. Yet previous work (Armbruster et al., 2020) that took into account diffusion, suggested potentially slower rise time dynamics. More importantly, the deconvolved waveforms do not match the shapes of the EPSCs (figures 5 and supp 6-2).What is the aim of the deconvolution? It was not clear from the text, but I assume it shows iGluSnFR binding to glutamate - in which case the slow waveforms are indicative of extrasynaptic iGluSnFR activation.

The deconvolution analysis was mainly used to recover the average responses to stimuli in the train without contamination by previous responses (see also Taschenberger et al. 2016, their figure 6).

We did also try to use the average singular response instead of the exponential fit as a kernel for the (Wiener) deconvolution analysis, which more closely resembled the observed (fast) rise. Unfortunately, this led to markedly worse results, likely because of the noise levels in the measurements. We believe that it would be beneficial to model the rise of the signal more precisely if glutamate imaging data is acquired at higher framerates.

The broad wave forms may be due to extrasynaptic binding of glutamate, but we also note that each frame corresponds to ~10ms and there is only ~10 data points between stimuli, so the responses are unlikely to be as sharp as eEPSCs.

However, I suppose that the more interesting question is whether iGluSnFR could be deconvolved to reveal the underlying release events, similar to how calcium signals can be used to inform about single action potentials.

We agree that it would be particularly interesting to use a "mini iGluSnFR" signal to deconvolve the resulting traces. Unfortunately, we failed to detect iGluSnFR signals reporting individual release events at this time, preventing this kind of analysis.

1. I suggest referencing and discussing (Aggarwal et al., 2022; Srivastava et al., 2022) . These highly relevant papers analyzed iGluSnFR to probe synaptic release.

References:

Aggarwal, A., Liu, R., Chen, Y., Ralowicz, A. J., Bergerson, S. J., Tomaska, F., Hanson, T. L., Hasseman, J. P., Reep, D., Tsegaye, G., Yao, P., Ji, X., Kloos, M., Walpita, D., Patel, R., Mohr, M. A., Tilberg, P. W., Mohar, B., Team, T. G. P., . . . Podgorski, K. (2022). Glutamate indicators with improved activation kinetics and localization for imaging synaptic transmission. bioRxiv, 2022.2002.2013.480251. https://doi.org/10.1101/2022.02.13.480251

Armbruster, M., Dulla, C. G., & Diamond, J. S. (2020). Effects of fluorescent glutamate indicators on neurotransmitter diffusion and uptake. Elife, 9. https://doi.org/10.7554/eLife.54441

Srivastava, P., de Rosenroll, G., Matsumoto, A., Michaels, T., Turple, Z., Jain, V., Sethuramanujam, S., Murphy-Baum, B. L., Yonehara, K., & Awatramani, G. B. (2022). Spatiotemporal properties of glutamate input support direction selectivity in the dendrites of retinal starburst amacrine cells. Elife, 11. https://doi.org/10.7554/eLife.81533

We thank the reviewer for the suggestions. Some of these studies were not available when we first drafted the manuscript. We now added a section discussing these studies starting on line 466:

Optimizing the imaging technique may reduce noise level, while the development of improved GEGIs could improve the signal to a level, at which spontaneous release events can be identified reliably in the cochlear nucleus. In retinal slices, where quantal events have been reliably observed with two-photon imaging, temporal deconvolution was successfully employed to estimate release rates from iGluSnFR signal (Srivastava et al., 2022; James et al., 2019). Subcellular targeting of iGluSnFR variants to the postsynaptic membrane may reduce measurement errors introduced by contributing extrasynaptic iGluSnFR signal and improve spatial resolution of glutamate imaging data(Hao et al., 2023; Aggarwal et al., 2022).

Referees cross-commenting

I also agree with the comments made by other reviewers!

Significance

Overall, this study addresses an important problem in basic neuroscience research. With the developing reliance on optical measurement of neuronal function, it is important to understand the impact of the indicators on physiological function and the limitations of the technique. The study is well-executed and will be informative to neuroscientists performing optical glutamate recording to study single-cell and circuit function in and beyond the auditory system.

Thank you so much for your paper! Metabolism of amino acids is extremely important to study but also very complex. It's also a really vast field so I really appreciate it when scientists decide to take a deep dive and uncover the existing metabolic pathways. Kudos for that! As excited as I am about L-amino acids, I'm even more excited to understand the metabolism of D-amino acids. I was wondering if you have considered applying your experimental approach to understand the metabolic pathway for D-arginine? May be also other D-amino acids? I think we know little about the metabolism of D-amino acids in B. subtilis and about the regulation of the metabolic enzymes. Thank you for your time!

Author Response

Reviewer #1 (Public Review):

It is well established that valuation and value-based decision-making is context-dependent. This manuscript presents the results of six behavioral experiments specifically designed to disentangle two prominent functional forms of value normalization during reward learning: divisive normalization and range normalization. The behavioral and modeling results are clear and convincing, showing that key features of choice behavior in the current setting are incompatible with divisive normalization but are well predicted by a non-linear transformation of range-normalized values.

Overall, this is an excellent study with important implications for reinforcement learning and decision-making research. The manuscript could be strengthened by examining individual variability in value normalization, as outlined below.

We thank the Reviewer for the positive appreciation of our work and for the very relevant suggestions. Please find our point-by-point answer below.

There is a lot of individual variation in the choice data that may potentially be explained by individual differences in normalization strategies. It would be important to examine whether there are any subgroups of subjects whose behavior is better explained by a divisive vs. range normalization process. Alternatively, it may be possible to compute an index that captures how much a given subject displays behavior compatible with divisive vs. range normalization. Seeing the distribution of such an index could provide insights into individual differences in normalization strategies.

Thank you for pointing this out, it is indeed true that there is some variability. To address this, and in line with the Reviewer’s suggestion, we extracted model attributions per participant on the individual out-of-sample log-likelihood, using the VBA_toolbox in Matlab (Daunizeau et al., 2014). In experiment 1 (presented in the main text), we found that the RANGE model accounted for 79% of the participants, while the DIVISIVE model accounted for 12%. The relative difference was even higher when including the RANGEω model in the model space: the RANGE and RANGEω models account for a total of 85% of the participants, while the DIVISIVE model accounted only for 5%.

In experiment 2 (presented in the supplementary materials), the results were comparable (see Figure 3-figure supplement 3: 73% vs 10%, 83% vs 2%).

To provide further insights into the behavioral signatures behind inter-individual differences, we plotted the transfer choice rates for each group of participants (best explained by the RANGE, DIVISIVE, or UNBIASED models), and the results are similar to our model predictions from Figure 1C:

Author Response Image 1. Behavioral data in the transfer phase, split over participants best explained by the RANGE (left), DIVISIVE (middle) or UNBIASED (right) model in experiment 1 (A) and experiment 2 (B) (versions a, b and c were pooled together).

To keep things concise, we did not include this last figure in the revised manuscript, but it will be available for the interested readers in the Rebuttal letter.

One possibility currently not considered by the authors is that both forms of value normalization are at work at the same time. It would be interesting to see the results from a hybrid model. R1.2 Thank you for the suggestion, we fitted and simulated a hybrid model as a weighted sum between both forms of normalization:

First, the HYBRID model quantitatively wins over the DIVISIVE model (oosLLHYB vs oosLLDIV : t(149)=10.19, p<.0001, d=0.41) but not over the RANGE model, which produced a marginally higher log-likelihood (oosLLHYB vs oosLLRAN : t(149)=-1.82, p=.07, d=-0.008). Second, model simulations also suggest that the model would predict a very similar (if not worse) behavior compared to the RANGE model (see figure below). This is supported by the distribution of the weight parameter over our participants: it appears that, consistently with the model attributions presented above, most participants are best explained by a range-normalization rule (weight > 0.5, 87% of the participants, see figure below). Together, these results favor the RANGE model over the DIVISIVE model in our task.

Out of curiosity, we also implemented a hybrid model as a weighted sum between absolute (UNBIASED model) and relative (RANGE model) valuations:

Model fitting, simulations and comparisons slightly favored this hybrid model over the UNBIASED model (oosLLHYB vs oosLLUNB: t(149)=2.63, p=.0094, d=0.15), but also drastically favored the range normalization account (oosLLHYB vs oosLLRAN : t(149)=-3.80, p=.00021, d=-0.40, see Author Response Image 2).

Author Response Image 2. Model simulations in the transfer phase for the RANGE model (left) and the HYBRID model (middle) defined as a weighted sum between divisive and range forms of normalization (top) and between unbiased (no normalization) and range normalization (bottom). The HYBRID model features an additional weight parameter, whose distribution favors the range normalization rule (right).

To keep things concise, we did not include this last figure in the revised manuscript, but it will be available for the interested readers in the Rebuttal letter.

Reviewer #2 (Public Review):

This paper studies how relative values are encoded in a learning task, and how they are subsequently used to make a decision. This is a topic that integrates multiple disciplines (psych, neuro, economics) and has generated significant interest. The experimental setting is based on previous work from this research team that has advanced the field's understanding of value coding in learning tasks. These experiments are well-designed to distinguish some predictions of different accounts for value encoding. However there is an additional treatment that would provide an additional (strong) test of these theories: RN would make an equivalent set of predictions if the range were equivalently adjusted downward instead (for example by adding a "68" option to "50" and "86", and then comparing to WB and WT). The predictions of DN would differ however because adding a low-value alternative to the normalization would not change it much. Would the behaviour of subjects be symmetric for equivalent ranges, as RN predicts? If so this would be a compelling result, because symmetry is a very strong theoretical assumption in this setting.

We thank the Reviewer for the overall positive appraisal concerning our work, but also for the stimulating and constructive remarks that we have addressed below. At this stage, we just wanted to mention that we also agree with the Reviewer concerning the fact that a design where we add "68" option to "50" and "86" would represent also an important test of our hypotheses. This is why we had, in fact, run this experiment. Unfortunately, their results were somehow buried in the Supplementary Materials of our original submission and not correctly highlighted in the main text. We modified the manuscript in order to make them more visible:

Behavioral results in three experiments (N=50 each) featuring a slightly different design, where we added a mid value option (NT68) between NT50 and NT87 converge to the same broad conclusion: the behavioral pattern in the transfer phase is largely incompatible with that predicted by outcome divisive normalization during the learning phase (Figure 2-figure supplement 2).

Reviewer #3 (Public Review):

Bavard & Palminteri extend their research program by devising a task that enables them to disassociate two types of normalisation: range normalisation (by which outcomes are normalised by the min and max of the options) and divisive normalisation (in which outcomes are normalised by the average of the options in ones context). By providing 4 different training contexts in which the range of outcomes and number of options vary, they successfully show using 'ex ante' simulations that different learning approaches during training (unbiased, divisive, range) should lead to different patterns of choice in a subsequent probe phase during which all options from the training are paired with one another generating novel choice pairings. These patterns are somewhat subtle but are elegantly unpacked. They then fit participants' training choices to different learning models and test how well these models predict probe phase choices. They find evidence - both in terms of quantitive (i.e. comparing out-of-sample log-likelihood scores) and qualitative (comparing the pattern of choices observed to the pattern that would be observed under each mode) fit - for the range model. This fit is further improved by adding a power parameter which suggests that alongside being relativised via range normalisation, outcomes were also transformed non-linearly.

I thought this approach to address their research question was really successful and the methods and results were strong, credible, and robust (owing to the number of experiments conducted, the design used and combination of approaches used). I do not think the paper has any major weaknesses. The paper is very clear and well-written which aids interpretability.

This is an important topic for understanding, predicting, and improving behaviour in a range of domains potentially. The findings will be of interest to researchers in interdisciplinary fields such as neuroeconomics and behavioural economics as well as reinforcement learning and cognitive psychology.

We thank Prof. Garrett for his positive evaluation and supportive attitude.

Author Response

Reviewer #2 (Public Review):

Granell et al. investigated genetic factors underlying wheezing from birth to young adulthood using a robust data-driven approach with the aim of understanding the genetic architecture of different wheezing phenotypes. The association of 8.1 million single nucleotide polymorphisms (SNPs) with wheeze phenotypes derived from birth to 18 years of age was evaluated in 9,568 subjects from five independent cohorts from the United Kingdom. This meta-genome-wide association study (GWAS) revealed the suggestive association of 134 independent SNPs with at least one wheezing subtype. Among these, 85 genetic variants were found to be potentially causative. Indeed, some of these were located nearby well-known asthma loci (e.g., the 17q21 chromosome band), although ANXA1 was revealed for the first time to play an important role in early-onset persistent wheezing. This was strongly supported by functional evidence. One of the top ANXA1 SNPs associated with wheezing was found to be potentially involved in the regulation of the transcription of this gene due to its location at the promoter region. This polymorphism (rs75260654) had been previously evidenced to regulate the ANXA1 expression in immune cells, as well as in pulmonary cells through its association as an eQTL. Protein-protein network analyses revealed the interaction of ANXA1 with proteins involved in asthma pathophysiology and regulation of the inflammatory response. Additionally, the authors conducted a murine model, finding increased anxa1 levels after a challenge with house dust mite allergens. Mice deficient in anxa1 showed decreased lung function, increased eosinophilia, and Th2 cell levels after allergen stimulation. These results suggest the dysregulation of the immune response in the lungs, eosinophilia, and Th2-driven exacerbations in response to allergens as a result of decreased levels of anxa1. This coincides with evidence of lower plasmatic ANXA1 levels in patients with uncontrolled asthma, suggesting this locus is a very promising candidate as a target of novel therapeutic strategies.

Limitations of this piece of work that need to be acknowledged:

(1) the manual and visual inspection of Locus Zoom plots for the refinement of association signals and identification of functional elements does not seem to be objective enough;

This is an important observation and we have now added the following text in the Discussion which can be found on lines 400-2 Revised Main Manuscript:

“Finally, the manual and visual inspection of Locus Zoom plots for the refinement of association signals and identification of functional elements was an objective approach which might have undermined the findings.“

(2) the sample size is limited, although the statistical power was improved by the assessment of very accurate disease sub-phenotype;

This point was already mentioned as a limitation and it can now be found in lines 349-365 Revised Main Manuscript:

“By GWAS standards, our study is comparatively small and may be considered to be underpowered. The sample size may be an issue when using an aggregated definition (such as “doctor-diagnosed asthma”) but is less likely to be an issue when primary outcome is determined by deep phenotyping. This is indirectly confirmed in our analyses. Our primary outcome was derived through careful phenotyping over a period of more than two decades in five independent birth cohorts, and although comparatively smaller than some asthma GWASs, our study proved to be powered enough to detect previously identified key associations (e.g. chr17q21 locus). Precise phenotyping has the potential to identify new risk loci. For example, a comparatively small GWAS (1,173 cases and 2,522 controls) which used a specific subtype of early-onset childhood asthma with recurrent severe exacerbations as an outcome, identified a functional variant in a novel susceptibility gene CDHR3 (SNP rs6967330) as an associate of this disease subtype, but not of doctor-diagnosed asthma(51). This important discovery was made with a considerably smaller sample size but using a more precise asthma subtype. In contrast, the largest asthma GWAS to date had a ~40-fold higher sample size(7), but reported no significant association between CDHR3 and aggregated asthma diagnosis. Therefore, with careful phenotyping, smaller sample sizes may be adequately powered to identify larger effect sizes than those in large GWASs with broader outcome definitions(52).”

(3) association signals with moderate significance levels but with strong functional evidence were found;

We do not think of this as a limitation but as a strength. We were able to support our genetic results with evidence from experimental mouse models.

(4) no direct replication of the findings in independent populations including diverse ancestry groups was described.

This point was already mentioned as a limitation and it can now be found in lines 375-391 and 392-399 Revised Main Manuscript.

“We are cognisant that there may be a perception of the lack of replication of our GWAS findings. We would argue that direct replication is almost certainly not possible in other cohorts, as phenotypes for replication studies should be homogenous(56). However, there is a considerable heterogeneity in LCA-derived wheeze phenotypes between studies, and although phenotypes in different studies are usually designated with the same names, they differ between studies in temporal trajectories, distributions within a population, and associated risk factors(57). This heterogeneity is in part consequent on the number and the non-uniformity of the timepoints used, and is likely one of the factors responsible for the lack of consistent associations of discovered phenotypes with risk factors reported in previous studies(58). This will also adversely impact the ability to identify phenotype-specific genetic associates. For example, we have previously shown that less distinct wheeze phenotypes in PIAMA were identified compared to those derived in ALSPAC(59). Thus, phenotypes that are homogeneous to those in our study almost certainly cannot readily be derived in available populations. This is exemplified in our attempted replication of ANXA1 findings in PIAMA cohort (see OLS, Table E12). In this analysis, the number of individuals assigned to persistent wheezing in PIAMA was small (40), associates of this phenotype differed to those in STELAR cohorts, and the SNPs’ imputation scores were low (<0.60), which meant the conditions for replication were not met.”

“Our study population is of European descent, and we cannot generalize the results to different ethnicities or environments. It is important to highlight the under-representation of ethnically diverse populations in most GWASs(9). To mitigate against this, large consortia have been formed, which combine the results of multiple ethnically diverse GWASs to increase the overall power to identify asthma-susceptibility loci. Examples include the GABRIEL(6), EVE(60) and TAGC(7) consortia, and the value of diverse, multi-ethnic participants in large-scale genomic studies has recently been shown(61). However, such consortia do not have the depth of longitudinal data to allow the type of analyses which we carried out to derive a multivariable primary outcome.”

Nonetheless, the robustness and consistency of the findings supported by different analytical and experimental layers is the major strength of this study.

The authors successfully achieved the aims of the study, strongly supported by the results presented. This study not only provides an exciting novel locus for wheezing with potential implications in the development of alternative therapeutic strategies but also opens the path for better-powered research of asthma genetics, focused on accurate disease phenotypes derived by innovative data-driven approaches that might speed up the process to disentangle the missing heritability of asthma, making use of still useful GWAS approaches.

Author Response

Reviewer #2 (Public Review):

The manuscript by Mohebi et al. examines a critical open question regarding the interaction of cholinergic interneurons of the striatum and transmitter release from dopaminergic axons in behaving animals. Activation of cholinergic interneurons in the striatum can evoke dopamine release in brain slices and in vivo as measured with voltammetry. However, it remains an open question in what context and to what extent this acetylcholine-mediated dopamine occurs in behaving animals. Here, the authors argue that CIN activity triggers dopamine release in the nucleus accumbens which encodes the motivation to obtain a reward through increasing "ramps" of dopamine release. Their data suggest that the ramps are not reflected in the firing of dopaminergic neurons. Rather, they provide compelling evidence that the ramps of dopamine release correlate with ramps in cholinergic interneuron activity as measured with GCaMP6. What's more, the authors show that ACh-mediated dopamine release has no paired-pulse depression, a striking result that differs from all prior ex vivo brain slice data. The manuscript is extremely well written and the data are of very high quality. Overall, this study represents an important step forward in our understanding of how ACh-mediated dopamine release regulates behavior, and more broadly how axons can generate behaviors independently from somatic activity.

Major comments

1) The complete absence of any short-term plasticity in CIN-mediated dopamine release is a striking result that is important for the field. The authors should strengthen this result with additional quantitative analysis demonstrating the lack of STP. They have analyzed paired-pulse ratios, but they should analyze this for stimuli at the higher frequencies (4 Hz, etc) that are more physiologically relevant. For example, Fig 1e shows a CIN-evoked DA release at many optically-stimulated frequencies. The authors should quantify short-term plasticity by generating fits of the single stimulus signal and comparing the mathematical sum predicted from 4 stim DA signals at different frequencies to the recorded data. A similar analysis has been done with Ca signals (Koester and Sakmann, 2000).

Thank you for this very helpful suggestion. We have performed this analysis as recommended, and now confirm the lack of STP even at the higher frequencies (see new Supplementary Figure 1).

2) The authors show that optical activation of CINs results in DA release as measured by dLight. To clearly establish that these signals are generated by DA release driven by nicotinic receptors (and not a partial effect of some unknown artifact), it would be useful to show that the optical CIN-evoked dLight signals shown in Fig. 1 are inhibited by nicotinic receptor antagonists such as DHbE. This control experiment would significantly strengthen the result shown here.

We agree that combining drug manipulations with photometry would be useful, but as noted above this is not a methodology in our current technical repertoire.

3) Similarly, the authors show clear correlations between CIN activity and DA release during behavior. The authors should consider determining whether CINs play a causal role in triggering DA release during behavior. For example, does infusion of DHbE in the NAc prevent the light-mediated DA release during behavior? As an alternative hypothesis, some groups have been suggesting that CIN activity has almost no direct influence over DA. Therefore, testing whether a causal relationship exists between CINs and DA release would be an important experiment in addressing these two opposing viewpoints.

As noted above we are not currently able to combine drug manipulations with photometry in behaving animals.

4) The ramps that are described in this manuscript are an order of magnitude faster (increasing over 100s of milliseconds) than ramps described in other studies that occur over seconds. In fact, the two signals may be completely different functionally. Discussion of this topic would be helpful.

Dopamine ramps have indeed been reported over multiple different time scales, and as discussed in Berke 2018, this seems to reflect the duration of the approach behavior. We think further discussion of this topic is better saved for another paper, especially as we are now actively studying ramping over longer time scales (Krausz et al. 2023).

Reviewer #3 (Public Review):

This report by Mohebi et al. provides new answers to old questions by showing that the activity of striatal cholinergic interneurons (CINs) escalates progressively during specific reward-related behaviors and that this correlates with previously observed ramps in dopamine (DA) release in the nucleus accumbens core. The report is strong and provides evidence for the authors' hypothesis that DA ramps are independent of DA neuron activity, but are instead the result of CIN activity and corresponding acetylcholine (ACh) release. The authors further demonstrate that the fidelity of CIN activation and consequent driving of DA release is even more robust in vivo than observed ex vivo slice preparations, which is fundamental for understanding the role of ACh-DA interactions in behavior. The findings complement the authors' previous evidence ventral tegmental area (VTA) DA neuron firing patterns do not show a ramping pattern; the previously reported VTA data are appropriately included here (in Fig. 3) to illustrate the absence of VTA firing during the time-locked increases in CIN activity and DA release. The present studies stop short of showing a direct link between CIN activity and DA release, however, which would require examining DA release during behavior in the presence of an antagonist of nicotinic ACh receptors. The authors also extend the understanding of the regulation of DA release by acetylcholine (ACh) by showing that optical activation of CINs in vivo promotes DA release responses that do not attenuate with repetitive stimulation. This contrasts with previous results in ex vivo striatal slices in which ACh-evoked DA release has been found to decline progressively from rundown and/or receptor desensitization. The authors propose that in vivo, AChE may be more effective in curtailing local ACh levels than in slices because of the slightly lower temperature typically used for slice studies, as well as the use of superfusion that might facilitate some AChE washout (AChE inhibitors are still effective in slices, of course). Overall, the report not only provides evidence for the cellular substrate for DA ramps but also shows the robustness of ACh-driven DA release in vivo. A few points to strengthen the report are listed below.

1) The authors give a few details about how CINs were activated at the beginning of the results, but say only that DA dynamics were monitored using fiber photometry. Given that the methods are at the end, a brief summary should be given here to indicate whether this means direct monitoring of DA or indirect via GCaMP, for example. It would be helpful to note the sensor used in the abstract, as well. In this light, as it were, RdLight1 should be described upon the first mention.

We have now clarified in both abstract and text that we are using the direct DA sensor RdLight1.

2) The authors show that infusion of DHbE in the NAc likelihood of decisions to approach the center port, as did antagonism of DA receptors. This supports the authors' argument that ramping of CIN activity and consequent ACh release underlies observed ramps in DA release. However, to show a causal interaction requires testing whether the observed DA ramps are absent after DHbE infusion in the NAc, under the same conditions that attenuated behavior.

As noted above we are not currently able to combine drug manipulations with photometry in behaving animals.

3) In Fig. 3, the y-axis title for the upper panels should specify VTA, not simply "rate". This is stated in the legend, but should also be specified in the figure panel.

We have updated the y-axis titles in this figure.

4) A recent preprint in BioRxiv by AC Krok, NX Tritsch et al. shows a related correlation between ACh and DA release in vivo in a reward task, as well as differences in other conditions. This report shows also that cortical input to CINs indeed plays a role, as suggested in the concluding sections of the present report. Consideration of the data in the preprint in the context of the present results could be valuable for the field.

We have also noted those pre-prints with interest, even though they investigated different brain regions using different approaches. There are established differences between CIN-DA interactions in dorsal vs. ventral striatum that we suspect are relevant here. But given the rapid pace of developments in this subfield, we prefer not to speculate too much at this point and instead review the overall body of work once it is published.

Author Response

Reviewer #1 (Public Review):

This is a simulation study comparing the performance of two major approaches for dealing with “population structure” when carrying out Genome-wide Association Studies - Principal Component Analysis and Linear Mixed-effects Models - a subject of considerable practical importance. The author correctly notes that previous comparisons have been quite limited. In particular, any study not concluding that LMM was superior has relied on very simple models of structure.

The paper is clearly written and beautifully reviews the theoretical underpinnings (albeit in a manner that will be difficult to penetrate without deep knowledge of several fields). The simulations are well-designed and far better than previous studies. From a theoretical point of view, the work is somewhat limited by being strongly anchored in a very classical quantitative genetics framework that is focused on allele frequencies and inbreeding coefficients, and totally ignores coalescent theory, but this is a minor quibble. The simulations are limited by utilizing ridiculously small sample sizes by the standards of modern human GWAS. And of course, they do not include all the complexities of real data.

The quantitative genetics framework we used was ideal for motivating and interpreting LMMs in particular, since they model relatedness with a kinship matrix which consists of IBD probabilities, all of which arose from quantitative genetics.

We also added the following text to the discussion: “However, our conclusions are not expected to change with larger sample sizes, as cryptic family relatedness will continue to be abundant in such data, if not increase in abundance, and thus give LMMs an advantage over PCA (Henn et al., 2012; Shchur et al., 2018; Loh et al., 2018).”

The main conclusion of the study is that LMM really are generally superior - as expected on theoretical grounds. However, the authors do address whether switching to LMM really is practicable given the sample size and lack of data sharing that characterize human genetics. Nor is it clear whether the difference in performance matters in real life given that the entire framework used is an idealized one - the fact that real human data suffers from environmental confounders that are correlated with “ancestry” is not addressed, to take the most obvious example. That said, it is surely important to note that the approach routinely used by the majority of users (PCA with 10 PCs) is most used for historical reasons and has little theoretical or empirical justification.

We added simulations with environment effects correlated with ancestry, which we hope will make our study even more relevant as it does make our evaluations even more realistic than before. In the presence of environment effects, LMM without PCs remains among the best approaches, although occasionally LMM with PCs or PCA will perform slightly better. However, modeling environment directly (with the true variables) improves performance much more than by using PCs to model environment indirectly, so we believe that is not a strong reason for continuing to use PCs (in LMMs or otherwise) unless there is no choice.

We also added the following text to the discussion: “However, recent approaches not tested in this work have made LMMs more scalable and applicable to biobank-scale data (Loh et al., 2015; Zhou et al., 2018; Mbatchou et al., 2021), so one clear next step is carefully evaluating these approaches in simulations with larger sample sizes.” As stated earlier, we believe that the difference in performance between LMM and PCA will remain in larger sample sizes because cryptic relatedness is more prevalent in that setting.

We excluded the “lack of data sharing” point from our discussion because it does not align well with the goals of our manuscript. The current solution to the lack of data sharing is meta-analysis, but its use does not give PCA or LMM an inherent advantage, since it can be applied to the summary statistics of either (or even a combination of models, in theory). There is interesting recent work on “federated” PCA and LMM association (both versions exist), that allow a single model to be fit jointly to separate datasets (residing in different buildings across the world) as if they were combined into a single dataset. Thus, these issues do not explain or motivate why PCA or LMM should be used.

Reviewer #2 (Public Review):

Yao and Ochoa present a very nice paper examining the age-old question of whether LMM or PCA is a better way to adjust for structure (population, family, admixture). The authors provide a very nice and detailed overview of the previous research addressing this question, summarizing it in a table. They find that LMMs are generally better at accounting for population structure. However, I feel there are a couple of important factors that are missing. One is the consideration of environmental structure. Another is that the relationship between PCA and LMM is usually a bit more complicated in practice than depicted here, where the devil really lies in the details. Also, I think there are a couple of key reasons why LMMs haven’t been adapted as quickly as one might have expected, including case-control imbalance and cohort meta-analyses, which I feel the authors could point out. In fact, I believe LMMs have become sort of popular in recent years (e.g. Japan Biobank GWAS results).

We added environment simulations, which we agree was an important shortcoming of the previous version of our work.

We now discuss how the PCA and LMM connection can be more complicated in practice, but as the main difference is in how LD is handled, once that is correctly adjusted, PCs and random effects are still mostly modeling the same relatedness signals. Ultimately, our main conclusion is unchanged, namely that only LMMs can model family relatedness, which is their key advantage.

We briefly commented on case-control imbalance in our discussion (now made more clear), but since this involves binary traits, which we did not explicitly test in this work, it is out of scope.

Cohort meta-analysis does not influence whether to use PCA or LMM, since it can be performed with summary statistics from either model (and in theory even a combination of different models per cohort). The broad use of meta-analysis does not in itself prevent users from using PCA or LMM within individual cohorts. The use of meta-analysis is very interesting in its own right, but it is outside the scope of this work.

Reviewer #3 (Public Review):

This paper examines the relative performance of linear mixed models (LMMs), principal components (PCA), and their combination (PCA-LMM) for genetic association studies in human populations. The authors claim that previous papers examining this question are inadequate and that: (i) there remains confusion on which method is best and in which context, (ii) that the metrics used in previous evaluations were insufficient, and (iii) that the simulation settings used in previous papers were not comprehensive. To fix these problems the authors perform an extensive set of simulations within several frameworks and suggest two new metrics for evaluating performance.

Strengths:

The simulation framework used in this paper and the extensive number of simulations provide an opportunity to examine the relative properties of the three approaches (LMM, PCA, PCA-LMM) in a variety of contexts.

The parameters of the simulation framework are based on highly diverged populations, which is an increasingly common analysis choice that has not been examined in detail via simulation previously.

The evaluation metrics used in this paper are AUC and a test of the uniformity of the p-value distribution under the null. This is an improvement over some previous analyses which did not examine power and relied on less sensitive tests of type I error.

Weaknesses:

This paper has a limited set of population frameworks just like all papers before it. The breakdown of which method is best (LMM, PCA, PCA-LMM) will be a function of the simulation framework chosen.

Ameliorating this issue, we added additional simulations with low heritability and with environment effects. We are pleased to report that all of our conclusions hold at low heritability (h2 = 0.3), and for the most part under environment effects (which occasionally give LMM with PCs and PCA a small advantage, but often LMM with no PCs remains best, and we show PCs are no replacement for directly modeling these environment effects).

The frameworks chosen for this paper are certainly not comprehensive in contemporary human genetic studies. In fact, the authors make a number of unusual choices. For example, the populations in the simulated study have extremely large Fsts. While this is also a strength, the lack of more standard study designs is a weakness. More importantly, there is no simulation of family effects, which is the basis of many of the PCA-LMM papers reported in Table 1.

We now better motivate in the introduction our focus on association studies of multiethnic and admixed individuals, which are nowadays very common and which have greater FST values than earlier studies. In reference to higher simulated FSTs, we also now cite our recent work, which has found that many previous FST estimates are downwardly biased (Ochoa and Storey, 2021, 2019). We simulated data that was fit to each of our three real datasets using our unbiased methods, so those values that (understandably) appear high are actually more correct (for multiethnic populations such as those in 1000 Genomes, HGDP, etc) than previous estimates in the literature. In our previous work we also determined that only previous pairwise FST estimators are unbiased (under some conditions), and using a previous pairwise FST estimator (from Bhatia et al., 2013) we obtained equally high values between the most diverged human populations (values from a revised version of Ochoa and Storey, 2019 that isn’t on bioRxiv yet): In HGDP, the largest pairwise FST is 0.479, between Pima and PapuanSepik; In Human Origins, the largest estimate is 0.396, between Cabecar and Baining_Malasait; Lastly, in 1000 Genomes, the largest estimate is 0.135, between YRI and JPT. (1000 Genomes was generally less structured than HGDP and Human Origins, because the latter include more diverse populations.) Several previous estimates from the literature, all between one hunter-gatherer Sub-Saharan African subpopulation and one non-African subpopulation resulted in values of about 0.25 (Bowcock et al., 1991, Henn et al., 2011, Bergstrom et al., 2020). FST estimates are also greater from whole-genome sequencing versus array data (revised version of Ochoa and Storey, 2019).

Family (household) effects is a case where PCA is not expected to outperform LMM, though standard LMMs do not model this effect explicitly either and may not do much better. As this is a feature of family studies that ought to be absent in population studies (as usually only siblings are in the same household, and not more distant relatives), it is also not entirely relevant to the majority of our simulations. In these ways, including such a feature in our simulations does not align with the goals of this present work, but we agree this is an important framework that deserves more attention in future evaluations.

The discussion (and simulations) of LMM vs PCA, particularly LMMs with PCs as fixed effects misses the critical distinction of whether PCs are in-sample (in which case including PCs as fixed effects effectively serves as a preconditioner for the kinship matrix, speeding up iterative methods such as BOLT), or projections of individuals onto out-of-sample principal axes. There is also no discussion of LOO methods to address “proximal contamination”, also quite relevant in evaluating power as a function of the number of PCs.

We added the following to our discussion concerning out-of-sample PC projections: “We do not consider the case where samples are projected onto PCs estimated from an external sample (Prive et al., 2020), which is uncommon in association studies, and whose primary effect is shrinkage, so if all samples are projected then they are all equally affected and larger regression coefficients compensate for the shrinkage, although this will no longer be the case if only a portion of the sample is projected onto the PCs of the rest of the sample.”

We also added the following to the discussion concerning the LOCO approach: “Similarly, the leave-onechromosome-out (LOCO) approach for estimating kinship matrices for LMMs prevents the test locus and loci in LD with it from being modeled by the random effect as well, which is called”proximal contamination” (Lippert et al., 2011, Yang et al., 2014). While LOCO kinship estimates vary for each chromosome, they continue to model family relatedness, thus maintaining their key advantage over PCA.”

The same new discussion paragraph closes with the following thoughts concerning LOCO and related approaches: “LD effects must be adjusted for, if present, so in unfiltered data we advise the previous methods be applied. However, in this work, simulated genotypes do not have LD, and the real datasets were filtered to remove LD, so here there is no proximal contamination and LD confounding is minimized if present at all, so these evaluations may be considered the ideal situation where LD effects have been adjusted successfully, and in this setting LMM outperforms PCA. Overall, these alternative PCs or kinship matrices differ from their basic counterparts by either the extent to which LD influences the estimates (which may be a confounder in a small portion of the genome, by definition) or by sampling noise, neither of which are expected to change our key conclusion.”

Lastly, we added the following to a different discussion paragraph: “A different benefit for including PCs were recently reported for BOLT-LMM, which does not result in greater power but rather in reduced runtime, a property that may be specific to its use of scalable algorithms such as conjugate gradient and variational Bayes (Loh et al., 2018).”

There is no discussion/simulation of spatial/environmental effects or rare vs common PCs as raised in Zaidi et al 2020. There are some open questions here regarding relative performance the authors could have looked at. Same for LMMs with multiple GRMs corresponding to maf/ld bins and thresholded GRMs. For example, it would be helpful to know if multiple-GRM LMMs mitigate some of the problems raised in the Zaidi paper.

We added simulations with environment effects, which are based on a two-level hierarchy of population labels so they are spatial to the extent that these labels capture spatial relationships between populations. However, our small sample size data are not well suited to study rare variants and their structure, so its out of scope. (The sample size limitation is also covered in a new discussion paragraph.) We hope to tackle this very interesting question in future work.

We added the following paragraph to our discussion: “Another limitation of this work is ignoring rare variants, a necessity given our smaller sample sizes, where rare variant association is miscalibrated and underpowered. Using simulations mimicking the UK Biobank, recent work has found that rare variants can have a more pronounced structure than common variants, and that modeling this rare variant structure (with either PCA and LMM) may better model environment confounding, improve inflation in association studies, and ameliorate stratification in polygenic risk scores (Zaidi and Mathieson, 2020). Better modeling rare variants and their structure is a key next step in association studies.”

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Reply to the reviewers

Manuscript number: RC-2022-01586

Corresponding author(s): Hammond, Gerald

1. General Statements

Our manuscript details a novel homeostatic feedback loop for the master plasma membrane regulatory molecule, PI(4,5)P2. In this loop, the PIP4K family of PI(4,5)P2-synthesizing enzymes act in a novel, non-enzymatic capacity: they sense PI(4,5)P2 levels and directly inhibit the lipid’s synthesis by inhibiting the major enzyme involved in the terminal step of synthesis, PIP5K. The three reviewers seem largely convinced of our data, and provided detailed, insightful and plausible suggestions for revision, which we have now comprehensively provided. This includes substantial new experimental work, including the generation of genomically tagged cell lines to localize all endogenous PIP4K isoforms.

However, all three reviewers questioned the paper’s novelty and significance based on recent studies in the literature demonstrating PIP5K inhibition by PIP4Ks [refs 25 & 53 in the manuscript]. We feel that this is an inaccurate and somewhat unfair assessment of our findings, since it does not consider our central (and completely unprecedented) finding that PIP4Ks directly sense PI(4,5)P2 levels through low-affinity binding. As well as being a novel finding, this places the previously observed inhibition of PIP5K by PIP4Ks into a completely new paradigm consisting of a complete, enclosed homeostatic feedback loop. This was not demonstrated previously in the literature.

Of course, the reviewers’ convergent opinions almost certainly reflect a deficit in our articulation of the novel findings in the original manuscript. We have therefore revised the current version to more clearly emphasize our novel findings.

2. Point-by-point description of the revisions

Reviewer #1

__Summary: __In this manuscript, authors address how PIP4K regulates tonic plasma membrane (PM) PI(4,5)P2 levels which are generated by major PI(4,5)P2 synthesis enzyme, PIP5K by using PIP4K and PIP5K overexpressing cells or acutely manipulating PM PI(4,5)P2 levels by the chemically induced dimerization (CID) system. Additionally, authors assessed effect of direct interaction between PIP4K and PIP5K by using supported lipid bilayers (SLBs) and purified PIP4K and 5K. Authors also were successful in monitoring dynamics of endogenous PIP4K by using a split fluorescent protein approach. Through this study, authors propose a model of PI(4,5)P2 homeostatic mechanism that PIP4Ks sense elevated PM PI(4,5)P2 by PIP5Ks, are recruited to the PM, and bind to PIP5Ks to inhibit PIP5Ks activity.

# 1.1: Although authors mention methods of statistical analysis in materials and methods, they did not present the results of statistical analysis in the figures. The quantitative data should be presented with statistical analysis data, which is important for showing where convincing differences between treatment groups are found.

We agree that statistics are important to fully interpret the data; we have now included the results of statistical tests (non-parametric statistics were used, as the data are not normally distributed) with correction for multiple comparisons. Significant changes are denoted using asterisk notation in figs. 1A-C, 2B, 5B & 7A. The full results are now reported as tables:

Fig 1A = table 1; Fig 1B = table 2; Fig. 1C = table 3; Fig. 2B = table 4; Fig. 5B = table 5; Fig 7A = tables 6 & 7.

__#1.2a: __Fig. 1D. Fig. 1D and Fig. 3A should be presented together because these are exactly same set of cells and information of each PIP4K and PIP5K membrane localization could be important for understanding mechanisms of inhibitory effect of PIP4Ks.

We struggled when writing the manuscript to reconcile these data into a single figure. The manuscript flows from showing inhibition of PIP5Ks by PIP4Ks in living cells (figs. 1 & 2), then showing low affinity PI(4,5)P2 binding by endogenous PIP4Ks (figs. 3-6) and finally to a direct interaction between PIP4K and PIP5K (fig. 7). We therefore felt that reconciling the data showing attenuated PI(4,5)P2 synthesis with the interaction between PIP4Ks and PIP5Ks, despite being demonstrated in the same experiments, would disrupt the flow of the paper. We therefore request to leave the data in Figs. 2B and 7A, whilst remaining explicit that the data derive from a single experiment.

#1.2b: Authors claimed that over-expression of all three PIP4K isoforms were able to attenuate the elevated PM PI(4,5)P2 levels caused by PIP5K over-expression. However, in Fig. 3A, PIP4K2A was recruited to PM by both PIP5K1A and PIP5K1C but looks only attenuated PIP5K1A, but not PIP5K1C, overexpression mediated PM PI(4,5)P2 elevation (Fig. 1D). PIP4K2C was less recruited to the PM than PIP4K2A and 2B in PIP5K1A overexpressing cell (Fig. 3A) but PIP4K2A, B and C isoforms equally attenuated increase of PM PI(4,5)P2 in PIP5K1A overexpressing cell (Fig. 1D). It is likely that efficiency of inhibitory effect of each PIP4K isoform is different by co-overexpressed PIP5K isoform. These images should be more carefully documented with Fig. 1D and Fig. 3A together.

As the reviewer suggests, we have now expanded our description of these data in both results and discussion; firstly, for the attenuating effects on PI(4,5)P2 synthesis, we write on the 3rd paragraph of p4: “We also reasoned that co-expression of PIP4K paralogs with PIP5K might attenuate the elevated PI(4,5)P2 levels induced by the latter. Broadly speaking, this was true, but with some curious paralog selectivity (fig. 2B, statistics reported in table 4): PIP4K2A and PIP4K2B both attenuated PI(4,5)P2 elevated by PIP5K1A and B, but not (or much less so) PIP5K1C; PIP4K2C, on the other hand, attenuated PIP5K1A and was the only paralog to significantly attenuate PIP5K1C’s effect, yet it did not attenuate PIP5K1B at all.”

On the relative ability of PIP5Ks to localize PIP4Ks we focus on the key result, writing on the 2nd paragraph of p7: “When co-expressing EGFP-tagged PIP5Ks and TagBFP2-tagged PIP4K2s, we found that PIP5K paralogs’ PM binding is largely unaffected by PIP4K over-expression (fig. 7A, upper panel and table 6), whereas all three paralogs of PIP4K are strongly recruited to the PM by co-expression of any PIP5K (fig. 7A, lower panel and table 7)…”

And finally, we describe a more nuanced discussion of the possible implications for differential inhibition of PIP5K isoforms by PIP4Ks in the discussion, starting in the first paragraph on p. 11: “Despite minor differences in the ability of over-expressed PIP5K paralogs to recruit over-expressed PIP4K enzymes (fig. 7A), we observed major differences in the ability of PIP4K paralogs to inhibit PI(4,5)P2 synthesis when over-expressed alone (fig. 1C) or in combination with PIP5K (fig. 2B). It is unclear what drives the partially overlapping inhibitory activity, where each PIP5K paralog can be attenuated by 2 or 3 PIP4Ks. This is however reminiscent of the biology of the PIPKs, where there is a high degree of redundancy among them, with few unique physiological functions assigned to specific paralogs [49]. There may be hints of paralog-specific functions in our data; for example, enhanced PI(4,5)P2 induced by over-expressed PIP5K1C is only really attenuated by PIP4K2C (fig. 2B). This could imply a requirement for PIP4K2C in regulating PI(4,5)P2 levels during PLC-mediated signaling, given the unique requirements for PIP5K1C in this process [50,51]. Regardless, a full understanding of paralog selectivity will need to be driven by a detailed structural analysis of the interaction between PIP4Ks and PIP5Ks - which is not immediately apparent from their known crystal structures, especially since PIP4Ks and PIP5Ks employ separate and distinct dimerization interfaces [49].”

#1.3: Fig. 1F. It seems that PIP4K2A accelerated PIP5K, but not Mss4, dependent PI(4,5)P2 generation before PI(4,5)P2 reaches 28,000 lipids/um2. Is this significant? If so, why did this happen?

We have answered this question with a sentence added to the 1st paragraph on p 8: *“The ability of PIP4K to bind to PIP5K on a PI(4,5)P2-containing bilayer also potentially explains the slightly accelerated initial rate of PI(4,5)P2synthesis exhibited by PIP5K1A that we reported in fig. 2C, since PIP4K may initially introduce some avidity to the membrane interaction by PIP5K, before PI(4,5)P2 reaches a sufficient concentration that PIP4K-mediated inhibition is effective.” *

#1.4: Fig. 3B. In this figure, authors only presented images after Rapa treatment. Therefore, it is not clear what these results mean. Before Rapa treatment, where did bait proteins and NG2-PIP4K2C localize? If ePIP4K2C delta PM intensity (ER:PM/PM) increase, does that mean increase in ER:PM intensity or decrease in PM intensity? According to Figure legend, PI(4,5)P2 indicator TubbycR332H was co-transfected, but those images are not shown in the figure. Images of PI(4,5)P2 indicator also should be presented to show whether after Rapa treatment PI(4,5)P2 increased at ER-PM contact sites, because that could be critical for the conclusion that "The use of Mss4 ruled out an effect of enhanced PI(4,5)P2 generation at contact sites, since this enzyme increases PI(4,5)P2 as potently as PIP5K1A (Fig. 1A), yet does not cause recruitment of PIP4K2C". Is this conclusion consistent with Fig. 2F and G?

These data now appear in Fig. 7B. We have added images showing the pre-rapamycin state to the revised figure. The reference to tubby­cR332H co-expression was an error. In fact, the cells expressed the ER:PM contact site marker MAPPER, which allowed us to quantify ER:PM contact site localization before and after rapamycin induced capture of the baits at these sites. The revised figure appears as follows:

The failure of Mss4 to recruit endogenous PIP4K2C is entirely consistent with the old Fig. 2F and G (now 5A and C), since these show PIP4K interaction with PI(4,5)P2 containing lipid bilayers (in Fig. 5C, the PI(4,5)P2 was synthesized by Mss4). We demonstrated that Mss4 is unable to interact with PIP4K2A in Fig. 7D.

#1.5: Fig. 3C and D. Based on results of Fig. 3C and D, authors concluded that "PIP4K2C binding to PI(4,5)P2-containing SLBs was greatly enhanced by addition of PIP5K to the membranes, but not Mss4". I don't think Fig. 3C and D are comparable because experimental conditions are different. While lipid composition of SLB used in Fig. 3C was 2% PI(4,5)P2, 98% DOPC, in Fig. 3D, it was 4% PI(4,5)P2, 96% DOPC. And also, in Fig. 3C, PIP5K1A was added to SLB at the time about 50 sec, whereas in Fig. 3D, Mss4 was added at 600 sec. It seems that in Fig. 3D, PIP4K2A was already saturated on SLB before adding Mss4. These two experiments must be performed under the same conditions.

We have repeated these experiments (which now appear in Fig. 7C & D) under identical conditions, with the same result.

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#1.6: Overall results discussed in the text are very compressed referring readers to the 4 multi-panel complex figures with elaborate figure legends. While it is possible to figure out what the authors' studies and results are, it is quite a laborious process.

We have revised the manuscript to be less compressed and easier to read, with the data now organized as eight figures and the results section split into four sub-sections.

Minor comments:

#1.7: Fig. 2D. The purified 5-phosphatase used in Fig. 2D is INPP5E but described in figure legend and materials and methods ass OCRL. Which one is correct?

Purified OCRL was indeed used in the supported lipid bilayer experiments. The figure (now Fig. 4A) and legend have been corrected – thank you for spotting the error.

#1.8: Fig. 3B. Indicate which trace represents PIP5K1A, Lyn11 or Mss4.

The data now appears in Fig. 7B, with the traces separated into separate graphs for greater clarity (see response to #1.4).

#1.9: Fig. 4C. X-axis label. Is "Time (min)" correct? Or should it be "Time (sec)".

Thank you for spotting this typo. It should have indeed been seconds, and this is corrected in the new fig. 8C.

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Reviewer #1 (Significance (Required)): The finding that PIP4K itself is a low-affinity PI(4,5)P2 binding protein and sense increases of PM PI(4,5)P2 generated by PIP5K to control tonic PI(4,5)P2 levels by inhibiting PIP5K activity is a novel concept. However, inhibition of PIP5K by PIP4K and importance of the inhibitory effect of PIP4K in PI3K signaling pathway have previously been reported (ref 24). This reduces the novelty of the current work somewhat however, the authors do provide evidence for dual interactions of PIP4K (PIP2, PIP5K), which the previous report did not.

We appreciate the reviewer’s insightful comments and overall appreciation of our work. We agree that previous studies did not detect the dual interaction of PIP4Ks with PIP5Ks and PI(4,5)P2; as we argue strongly in the general comments, we think this actually fits as a complete, enclosed homeostatic feedback loop – which is a significant and novel finding.

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Reviewer #2

Summary: This paper proposes that the enzyme PIP4K2C is a negative regulator of the synthesis of PI(4,5)P2 and that it does so by dampening the activity of PIP5K which is the enzymatic activity responsible for producing the major pool of PI(4,5)P2 in cells.

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Reviewer #2 (Significance (Required)): Although the findings of the paper are presented as a major new advance, the observation that PIP4K might acts as a negative regulator of PIP2 synthesis has been previously presented in two previous publications. The significance of this paper is that it also shows the same point in another model system.

PIP4Ks Suppress Insulin Signaling through a Catalytic-Independent Mechanism

Diana G Wang 1, Marcia N Paddock 2, Mark R Lundquist 3, Janet Y Sun 3, Oksana Mashadova 3, Solomon Amadiume 3, Timothy W Bumpus 4, Cindy Hodakoski 3, Benjamin D Hopkins 3, Matthew Fine 3, Amanda Hill 3, T Jonathan Yang 5, Jeremy M Baskin 4, Lukas E Dow 6, Lewis C Cantley 7

PMID: 31091439; PMCID: PMC6619495;DOI: 10.1016/j.celrep.2019.04.070

and

Phosphatidylinositol 5 Phosphate 4-Kinase Regulates Plasma-Membrane PIP3 Turnover and Insulin Signaling.

Sharma S, Mathre S, Ramya V, Shinde D, Raghu P.Cell Rep. 2019 May 14;27(7):1979-1990.e7. doi: 10.1016/j.celrep.2019.04.084.PMID: 31091438

Both of these studies show that in cells lacking PIP4K, during signalling the levels of PIP2 rise much greater than in wild type cells. Indeed the Cantley lab paper (Wang et.al) have shown that this is likely due to an increase in PIP5K activity, using an in vitro assay. They have further disrupted the interaction between PIP4K and PIP5K and demonstrated the importance of this interaction in the enhanced levels of PIP2.

Respectfully, we disagree with this assessment, because we believe it doesn’t consider the novel, central findings we report: that PIP4Ks sense PI(4,5)P2 levels through direct interaction with the lipid, and that this is what facilitates PIP5K inhibition. These findings were not reported in the prior studies. Nonetheless, the studies are foundational for ours and were cited in our original manuscript (and are still, as refs 25 and 53).

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#2.1: Likewise although the authors have claimed that no mechanisms have claimed that there are no mechanisms reported to sense and downregulate PIP2 resynthesis. It is suggested that they read and consider the following recent paper which studies Pip2 resynthesis during GPCR triggered PLC signalling.

Kumari A, Ghosh A, Kolay S and Raghu P*. Septins tune lipid kinase activity and PI(4,5)P 2 turnover during G-protein-coupled PLC signalling in vivo. Life Sci Alliance. 2022 Mar 11;5(6):e202101293. doi: 10.26508/lsa.202101293. Print 2022 Jun.

We have now included a full discussion of this paper in the discussion starting on the last paragraph of p 9: “Since this paper was initially submitted for publication, another study has reported a similar homeostatic feedback loop in Drosophila photoreceptors, utilizing the fly homologue of septin 7 as the receptor and control center [38]. This conclusion is based on the observation that cells with reduced septin 7 levels have enhanced PIP5K activity in lysates, and exhibit more rapid PI(4,5)P2 resynthesis after PLC activation. However, changes in septin 7 membrane localization in response to acute alterations in PI(4,5)P2 levels, as well as direct interactions between PIP5K and septin 7, have yet to be demonstrated. Nevertheless, septin 7 has distinct properties as a potential homeostatic mediator; as a foundational member of the septin family, it is essential for generating all major types of septin filament [39]. Therefore, a null allele for this subunit is expected to reduce the prevalence of the septin cytoskeleton by half. Given that septin subunits are found in mammalian cells at high copy number, around ~106 each [29], and the fact that septins bind PI4P and PI(4,5)P2 [40,41], it is likely that septin filaments sequester a significant fraction of the PM PI4P and PI(4,5)P2 through high-avidity interactions. In addition, membrane-bound septins appear to be effective diffusion barriers to PI(4,5)P2 and other lipids [42]. We therefore speculate that septins may play a unique role in systems such as the fly photoreceptor with extremely high levels of PLC-mediated PI(4,5)P2 turnover: The septin cytoskeleton can act as a significant buffer for PI4P and PI(4,5)P2 in such systems, as well as corralling pools of the lipids for use at the rhabdomeres were the high rate of turnover occurs. This is in contrast to the role played by the PIP4Ks, where PI(4,5)P2 levels are held in a narrow range under conditions of more limited turnover, as found in most cells.”

__#2.2: __Likewise there are other earlier papers in the literature which have studied possible PIP2 binding proteins as sensors for this lipid.

We are only aware of a single, specific example of a similar negative feedback, which is discussed in the 3rdparagraph of p 10: “Curiously, although phosphatidylinositol phosphate kinases are found throughout eukarya, PIP4Ks are limited to holozoa (animals and closely related unicellular organisms) [47]. Indeed, we found the PIP5K from the fission yeast, Saccharomyces cerevisiae, does not interact with human PIP4Ks (fig. 7) and cannot modulate PI(4,5)P2 levels in human cells without its catalytic activity (fig. 1). This begs the question: how do S. cerevisiae regulate their own PI(4,5)P2 levels? Intriguingly, they seem to have a paralogous homeostatic mechanism: the dual PH domain containing protein Opy1 serves as receptor and control center [48], in an analogous role to PIP4K. Since there is no mammalian homolog of Opy1, this homeostatic mechanism appears to have appeared at least twice through convergent evolution. Combined with hints of a role for septins in maintaining PI(4,5)P2 levels [38], the possibility arises that there may yet be more feedback controls of PI(4,5)P2 levels to be discovered.”

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Technical standards: The work is done to a high technical standard.

#2.3: Does catalytically dead isoform of PIP4K2B and 2C also yield the same result as a catalytically dead version of PIP4K2A in Fig 1B?

In a word: yes. We have added these experiments, which are now presented in Fig. 2A:

The results are described in the results in the 2nd paragraph of p. 4: “To directly test for negative regulation of PIP5K activity by PIP4K in cells, we wanted to assay PI(4,5)P2 levels after acute membrane recruitment of normally cytosolic PIP4K paralogs. To this end, we triggered rapid PM recruitment of cytosolic, FKBP-tagged PIP4K by chemically induced dimerization (CID) with a membrane targeted FRB domain, using rapamycin [27]. As shown in fig. 2A, all three paralogs of PIP4K induce a steady decline in PM PI(4,5)P2 levels within minutes of PM recruitment. Catalytically inactive mutants of all three paralogs produce identical responses (fig. 2A).”

#2.4: The labelling on y-axis for PI(4,5)P2 biosensor intensity ratio is PM/cell at some places, PM/Cyt or PM/Cyto in some places. It is recommended to make it uniform across all the panels.

PM/Cyto was a typo, now corrected to PM/Cyt. PM/Cell and PM/Cyt are two subtly different metrics used to normalize PM fluorescence intensity across varying transient expression levels. This is clarified in the methods in the 3rdparagraph on p.22: “For confocal images, the ratio of fluorescence intensity between specific compartments was analyzed as described previously [59]. In brief, a custom macro was used to generate a compartment of interest specific binary mask through à trous wavelet decomposition[68]. This mask was applied to measure the fluorescence intensity within the given compartment while normalizing to the mean pixel intensity in the ROI. ROI corresponded to the whole cell (denoted PM/Cell ratio) or a region of cytosol (PM/Cyt), as indicated on the y axis of individual figures.”

#2.5: The claim that PI(4,5)P2 production is sufficient to recruit PIP4K2C to the PM can be ascertained further if one is able to do an experiment where PI(4,5)P2 is ectopically expressed in some compartment of the cell which is non-native to PI(4,5)P2 and as a consequence of this PIP4K2C is recruited to this non-native compartment.

We have now removed the assertion that PI(4,5)P2 is sufficient to localize PIP4Ks to the membrane, since our conclusion is that the coincident presence of PI(4,5)P2 and PIP5Ks in the PM is what ultimately localizes the PIP4Ks. We did not detect recruitment of endogenous PIP4Ks to lysosomes when ectopic PI(4,5)P2 synthesis was induced, although fluorescence levels are so low as to be inconclusive, and therefore not appropriate for inclusion in the manuscript.

#2.6: In the entire figure 2, to establish that PI(4,5)P2 is necessary and sufficient for PM localisation of PIP4K, PIP4K2C is used as the PIP4K isoform on the basis that it is highly abundant in HEK293 cells. But PIP4K2A is localised mainly at the plasma membrane and here we are discussing about PI(4,5)P2 regulation at the PM . Can experiments be done with isoforms 2A and 2B as well? Can acute depletion of PI(4,5)P2 lead to the membrane dissociation of the isoform 2A as well? This will help us in understanding if there is an isoform specific difference in sensing PI(4,5)P2 levels which will help us in targeting specific isoform as therapeutic targets.

We have now generated endogenously tagged PIP4K2A and PIP4K2B; these cell lines are characterized in the revised fig. 3:

With the dependence on PI(4,5)P2 for PM binding for all isoforms shown in fig. 4:

32 cells that were imaged across three independent experiments. (E) Depletion of PI(4,5)P2 causes NG2-PIP4K2C to dissociate from the membrane. As in C, NG2-PIP4K2C (blue) cells were transfected with FKBP-tagged proteins, TubbyC (orange) and Lyn11-FRB, scale bar is 2.5 µm; cells were stimulated with 1µM rapa, as indicated. TubbyC traces represent mean change in fluorescence intensity (Ft/Fpre) ± s.e. The NG2-PIP4K2C traces represent the mean change in puncta per µm2 ± s.e. of > 38 cells that were imaged across three independent experiments. " v:shapes="Text_x0020_Box_x0020_5">

And increased binding by elevated PI(4,5)P2 levels shown in fig. 5B:

The results are described in the accompanying results text “PIP4K are low affinity sensors of PM PI(4,5)P2”, pp.4-7. In short, endogenous PIP4K isoforms behave similarly with respect to PI(4,5)P2-dependent PM recruitment.

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#2.7: In Figure 1A, it is shown that overexpression of a catalytically dead PIP5K 1A/1B/1C is still able to increase PI(4,5)P2 levels. In the figure 2E, expression of homodimeric mutant of PIP5K domain which is a way to increase catalytic activity of PIP5K, increases PI(4,5)P2 levels which is consistent with the inferences from Fig, 1 , but what is surprising is a catalytically dead variant not being able to do so. Why is there a discrepancy between Fig. 1A and Fig. 2E? If the homodimeric mutant is the reason, then it is not clear in the explanation.

We have added the following clarification to the results on the second paragraph of p.6: “We next tested for rapid binding to acutely increasing PI(4,5)P2 levels in living cells, using CID of a homodimeric mutant PIP5K domain (PIP5K-HD), which can only dimerize with itself and not endogenous PIP5K paralogs [34]. This domain also lacks two basic residues that are crucial for membrane binding [35], and only elevates PM PI(4,5)P2 when it retains catalytic activity (fig. 5D), unlike the full-length protein (fig. 1A).” We currently do not fully understand why these well characterized residues of PIP5Ks are necessary for PM binding and inhibition by PIP4K. This is a focus of ongoing studies in the lab for the structural basis of PIP5K inhibition by PIP4K.

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#2.8: Show the loading control in Fig 2A western.

We have added the loading control using alpha tubulin in the revised fig. 3B.

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#2.9: In the figure 2D, in the legend OCRL is written. So, the labelling in the panel should also be changed to OCRL from INPP5E. It is intermixed.

Reviewer 1 also spotted this inconsistency (#1.7): Purified OCRL was indeed in the supported lipid bilayer experiments. The figure (now Fig. 4A) and legend have been corrected – thank you for spotting the error.

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#2.10: In the figure 2E, can the labelling be changed from HD to something more self-explanatory for homodimeric mutant of PIP5K domain?

We prefer to keep the “HD” notation in the revised figure 5D for brevity’s sake, but now define the abbreviation in the text in the second paragraph of p.6: “…a homodimeric mutant PIP5K domain (PIP5K-HD)…”.

#2.11: In Fig. 2E, PIP5K expression is acute and in Fig. 2F Mss4 expression is chronic, both of which is able to recruit PIP4K2C to the plasma membrane. How can a likewise argument be drawn out of these two experiments when one is acute and the other one is a chronic expression? It is suggested to do an FRB-FKBP experiment for Mss4 as well.

We agree with the reviewer that an FKBP-Mss4 would have been an excellent experiment. As can be seen from Fig. __1A, Mss4 is constitutively PM localized in mammalian cells. However, we were unable to identify a truncation of Mss4 that lost constitutive membrane binding whilst retaining catalytic activity. Therefore, we could only perform chronic overexpression as shown in __fig. 5B. The lack of an acute demonstration is why we went on to develop the PIP5K-HD constructs, results of which are reported in __fig. 5D. __

#2.12: In the text, Fig. 2G and 2H is written for PIP4K2C, but in the corresponding panels and legends, it is an assay for purified PIP4K2A on SLBs. Kindly resolve the discrepancy.

We thank the reviewer for spotting this discrepancy. PIP4K2A is the protein that was used in the SLB experiments now reported in fig. 5A & C and the accompanying results on pp.5-6. This is now corrected in the manuscript.

#2.13: Kindly explain a bit in detail why the baits were now targeted to ER-PM contact sites. It is not self-explanatory.

We have now added a more detailed description to the third paragraph of p. 7: “We therefore sought to distinguish between a direct PIP5K-PIP4K binding interaction versus PI(4,5)P2-induced co-enrichment on the PM. To this end, we devised an experiment whereby a bait protein (either PIP5K or control proteins) could be acutely localized to subdomains of the PM, with the same PI(4,5)P2 concentration. This was achieved using CID of baits with an endoplasmic reticulum (ER) tethered protein, causing restricted localization of the bait protein to ER-PM contact sites – a subdomain of the PM (fig. 7B).”

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#2.14: The conclusions for Fig. 3 most likely hints towards the possibility of PIP4K and PIP5K interaction being independent of PI(4,5)P2 levels. Well, Fig. 3C and 3D does suggest a direct interaction, but can other protein-protein interaction assays be used to establish the direct interaction of PIP4K with PIP5K such as FRET or Yeast two hybrid as assays scoring for interaction?

We respectfully diverge from the reviewer’s assessment of the data, presented in the revised fig. 7. Figs. 7A & B__show PIP4K and PIP5K interacting in the context of a PI(4,5)P2 replete PM; __fig. 7C shows this in the context of a PI(4,5)P2 replete SLB. Therefore, we make no assertion that the PIP4K/PIP5K is independent of PI(4,5)P2 levels. We also contend that the latter experiment is a more direct demonstration than a Y2H assay, or even FRET (which can occur among non-interacting proteins localized to a membrane surface, see e.g. 10.1074/jbc.m007194200).

#2.15: Conceptually a direct interaction can be explained to some extent from Fig. 3 but extending it to be an inhibitory interaction is not right without a direct experiment. Can an experiment be done with PI4P enriched SLB, wherein you put just PIP5K purified protein vs PIP5K+PIP4K combination and measure the % mol of PI(4,5)P2 produced using a probe. That will be suggestive of a negative interaction.

This is a great experiment, the results of which are reported in fig. 2C, described in the third full paragraph of p. 4: “To more directly examine inhibition of PIP5K by PIP4K, we tested activity of purified PIP5K1A on PI4P-containing supported lipid bilayers (SLBs). Addition of PIP4K2A exhibited delayed inhibition of PIP5K1A activity (fig. 2C): Once PI(4,5)P2 reached approximately 28,000 lipids/µm2 (~2 mol %), PIP5K dependent lipid phosphorylation slowed down, which doubled the reaction completion time (fig. 2C, right). In contrast, we observed no PIP4K dependent inhibition of Mss4 (fig. 2C, inset). These data recapitulate the prior finding that PIP4K only inhibited purified PIP5K in the presence of bilayer-presented substrate [25]. We therefore hypothesized that inhibition of PIP5K by PIP4K requires recruitment of the latter enzyme to the PM by PI(4,5)P2 itself.”

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__#2.15: __ In Figure 3B, the FRB tagged constructs are magenta coded and PIP4K2C is cyan. Kindly change the labelling of the FRB constructs on the y axis to magenta so that it goes with what is written in the legend. It will also be appreciated to show a colocalization quantification between the magenta (FRB constructs) and cyan (PIP4K2C) post rapamycin addition and not just the intensity for ER-PM recruited PIP4K2C.

These modifications and some additional points have been added in response to reviewer 1’s #1.4 to the revised fig. 7B. Note, we quantified the co-localization with an ER-PM contact site marker, MAPPER. Co-localization with the FRB-tagged construct would be misleading, because this construct is localized across the membrane at the start of the experiment and would thus have a high degree of co-localization. As can be seen from the inset graphs in the new analysis, however, all FRB-tagged constructs co-localize with MAPPER after rapamycin addition, but only FRB-PIP5K1A causes endogenous PIP4K2C to increase co-localization with this compartment.

# 2.16: Again, in the text , the description is written for PIP4K2C but in the result panel and legend (Fig. 3C and Fig. 3D), PIP4K2A is mentioned. Kindly resolve the discrepancy

We have corrected the results text on the last paragraph of p. 7: “Finally, we also demonstrate that PIP4K2A binding to PI(4,5)P2-containing supported lipid bilayers was greatly enhanced by addition of PIP5K to the membranes (fig. 7C), but not by Mss4 (fig. 7D).”

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# 2.17: In the Fig. 4B, it will be appreciated to show statistical significance in terms of R2 value for commenting on the linear response.

“Linear response” was not the best description of what we were trying to articulate in the revised fig. 8B; we have now amended the results in the 2nd paragraph of p.8 to read: “Of these, Tubbyc showed the largest degree of change in PM localization across all changes in PI(4,5)P2 levels (fig. 8B).”

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#2.18: Discussion can be in general a bit more detailed which is suggestive of future experiments to do that can shed more light on the interaction such as which residues in PIP4K interacts with PIP5K to negatively regulate it.

The revised manuscript contains a greatly expanded discussion, as described in detail in our responses to comments #1.2b, #2.1 and __#2.2. __

#2.19: In the discussion, more light can be shed on the fact that Mss4 in spite of being a 5- kinase is not negatively regulated by PIP4K and the fact that PIP4K is present only in metazoans suggests that this fine tuning of PI(4,5)P2 levels is specific to metazoans. Another insight could be in the direction, that Fig 4. tells PI3K, but not calcium signaling is modulated by this fine tuning and interestingly class I PI3K is also an enzyme specific to metazoans. Hence, unlike yeast, metazoans rely on growth factor signalling processes, hence regulation of PI(4,5)P2 by PIP4K and hence Class I PI3K and PI(3,4,5)P3 could be a process relevant to metazoans.

We have addressed the restriction of PIP4K to holozoa as described in our response to #2.2, wherein we describe a previously proposed paralogous mechanism in fungi. The reviewer’s point about the homeostatic process being related to class I PI3K signaling in growth control of multicellular organisms is interesting, but the presence of the PIP4Ks in some unicellular organisms complicates this view. We are of the view that a discussion of this important topic is a little nuanced for inclusion in the current manuscript.

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Reviewer #3

__Summary: __Using state of the art imaging techniques the authors try to address how cells sense PI(4,5)P2 levels and regulate PIP5Ks to maintain an optimal level since any dysregulation of PI(4,5)P2 levels can have significant effects on the functioning of the cell and led to numerous disease states, such as cancers.

The key conclusions are convincing and importantly validate previous disputed findings made by Wang et al. (Cell Reports 2019) using different and more rigorous methods, however unfortunately due to the Wang et al publication the overall novelty of this study is lacking. A suggestion to the authors is to state/explain with text more clearly how their findings are more precise and higher quality than the previous report and why their findings are necessary and significant to drive the field forward.

We have revised the manuscript to more clearly state our novel finding that PIP4Ks are PI(4,5)P2 sensing proteins that inhibit PIP5Ks on the membrane in a PI(4,5)P2-dependent manner, which was not previously described in the literature.

Further, experiments in the study were performed in vitro in cultured cells using overexpression methods making the physiological significance a bit unclear and the enthusiasm of the main discovery dampened. With that being said these findings are worthy of publication in order to advance the field and understanding of how the PIP kinase families are regulated and maintain PIP2 homeostasis which is important for life.

We feel that this assessment is slightly unfair, since most of the key experiments have been validated using purified proteins in supported lipid bilayers, and endogenous proteins were studied using genomic tagging approaches, rather than over-expression.

Minor and easily addressable experiments should be performed by the authors the following. Further, many of these experimental issues can easily go in supplemental materials

#3.1: Include western blots for the constructs to compare expression levels.

We agree that it is important to take into account differences in expression levels for the experiments presented in fig. 1. However, since these are single cell assays, Western blotting of whole populations of transiently transfected cells is not the best control. Instead, having acquired the images under consistent excitation and detection parameters, we compared the fluorescence intensity, expressed as relative expression in Fig. 1A and C, which is discussed in the results text in the first two paragraphs of the results on p. 3: “Notably, expression of the catalytically inactive mutants was usually somewhat less strong compared to the wild-type enzymes, yet effects on PI(4,5)P2 levels were similar (fig. 1A).” and “Again, differences in expression level between isoforms do not explain differences in activity, since all achieved comparable expression levels as assessed by fluorescence intensity (fig. 1C).”

#3.2: For Figure 1A, what is the source of the observed increase in PI(4,5)P2, how do the authors take into account the role of endogenous PIP5Ks?

We added a new experiment in the revised Fig. 1B showing that the increased PI(4,5)P2 occurs at the expense of PM PI4P:

This is described in the first paragraph of the results on p.3: “PI(4,5)P2 levels are expected to increase at the expense of PM PI4P levels when over-expressing any of the three isoforms of human PIP5K (A-C) or the single paralog from the budding yeast, Saccharomyces cerevisiae (Mss4). Indeed, this was precisely what we observed (fig. 1A and B, statistics reported in tables 1 and 2).”

The role for endogenous PIP5Ks is clarified on the sentence that spans pp. 3-4: “We therefore reasoned that saturation of endogenous, inhibitory PIP4K molecules by PIP5K over-expression, regardless of catalytic activity of the PIP5K, would free endogenous, active PIP5K enzyme from negative regulation (fig. 1D).”

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#3.3: For Figure 1B, could the authors comment on the intracellular distribution of PI(4,5)P2. How are they able to reliably distinguish their signal between plasma membrane and intracellular localizations and conclude that PIP2 on the plasma membrane is decreased?

As detailed in the now expanded methods section covering image analysis on p. 22, our analysis specifically quantifies fluorescence in the plasma membrane.

#3.4: Please include statistics for all image- based quantitation analysis.

We have added details of statistical analysis and tabulated the results, as detailed in our response to __#1.1. __

__#3.5: __ Could the authors comment on the ability of PIP4K to have affinity for its own product? How does PIP4K sense membrane PI(4,5)P2 since these kinases are mostly cytoplasmic?

We have added a comment to the 1st paragraph of the Discussion on p.9: “PIP4K’s low affinity and highly co-operative binding to PI(4,5)P2 makes it an excellent sensor for tonic PI(4,5)P2 levels. It is poised to sense PI(4,5)P2generated in excess of the needs of the lipids’ legion effector proteins, ensuring these needs are met but not exceeded. Nevertheless, the relatively low PIP4K copy number of around 2.5 x 105 per cell [29] is a small fraction of the total PI(4,5)P2 pool, estimated to be ~107 [33], ensuring little impact on the capacity of the lipid to interact with its effectors.”

__#3.6: __Do the authors have any other experiments to substantiate the binding of the two PIP kinases, similar to the Wang et al findings? Is the N-term motif required? Is it possible to disrupt that interaction and show the phenotype?

We do not have additional, conclusive experiments to share at this time, and believe that characterization of the inhibitory interaction is beyond the scope of the current manuscript. We do however add a comment on this topic to the 1st paragraph of p. 11: “Regardless, a full understanding of paralog selectivity will need to be driven by a detailed structural analysis of the interaction between PIP4Ks and PIP5Ks - which is not immediately apparent from their known crystal structures, especially since PIP4Ks and PIP5Ks employ separate and distinct dimerization interfaces [50].”

#3.7: With the overexpression studies in Figure 1, do the authors see any changes in signaling when they just overexpress PIP5Ks versus in combination with PIP4Ks to show that the changes in plasma membrane PI(4,5)P2 can affect downstream signaling?

We agree with the reviewer that attenuating PIP5K-mediated PI(4,5)P2 increases with PIP4K should affect downstream signaling. However, we believe that these will not add additional insight compared to the already included experiments (fig. 8), whereby signaling output in response to graded changes in PI(4,5)P2 levels was investigated.

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Reviewer #3 (Significance (Required)): Overall, as mentioned above because of the 2019 Wang et al report the novelty is diminished, however using completely alternate methods and sophisticated microscopy this body of work indeed advances the field and provides further believable evidence of the PIP kinase families communicating in higher organisms which is required to maintain PIP2 levels shedding light on many of the findings that were previously unexplained surrounding the PIP4K studies. Further, the use of biosensors to describe these findings are new and will enable others in the field to begin to use such tools to investigate potential crosstalk between other lipid kinases.

As we argued in the general comments, we do feel that this evaluation misses the key finding that PIP4Ks are PI(4,5)P2 sensors, and that this regulates PIP5K regulation as part of a feedback loop.

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

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Reply to the reviewers

Manuscript number: RC-2022-01723

Corresponding author(s): Daphne Avgousti, Srinivas Ramachandran

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

Summary This study by Lewis et al. examines the role of heterochromatin in the nuclear egress of herpesvirus capsids. They show that heterochromatin markers macroH2A1 and H3K27me3 are enriched at specific genome regions during the infection. They also show that when macroH2A1 is removed or H3K27me3 is depleted (both of which reduce the amount of heterochromatin at the nuclear periphery), the capsids are not able to egress as effectively. This is interesting since it could be argued that heterochromatin acts as a hindrance to the transport of viral capsids to the nuclear envelope and that the loss of it would allow capsids to reach the nuclear envelope more easily. However, this paper seems to show that heterochromatin formation, on the contrary, is necessary for efficient egress. Overall, the study seems comprehensive. The methodology is solid, and the experiments are very well controlled. However, some issues need to be addressed before publication.

Major comments

1) In line 49, the authors state, "Like most DNA viruses, herpes simplex virus (HSV-1) takes advantage of host chromatin factors both by incorporating histones onto its genome to promote gene expression and by reorganizing host chromatin during infection". In addition, HSV1 expression can be hindered by the host's interferon response via histone modifications. Ref. Johnson KE, Bottero V, Flaherty S, Dutta S, Singh VV, Chandran B. IFI16 restricts HSV-1 replication by accumulating on the HSV-1 genome, repressing HSV-1 gene expression, and directly or indirectly modulating histone modifications. PLoS Pathog. 2014 Nov 6;10(11):e1004503. doi: 10.1371/journal.ppat.1004503. Erratum in: PLoS Pathog. 2018 Jun 6;14(6):e1007113. PMID: 25375629; PMCID: PMC4223080.

We agree with the reviewer and have amended our text and added the reference. See line 57.

2) Reference 5 is misquoted in the sentence, "This redistribution of host chromatin results in a global increase in heterochromatin". In that reference, the amount of heterochromatin is not analyzed in any way. However, that particular paper shows that the transport of capsid through chromatin is the rate-limiting step in nuclear egress, which is important considering this study. Further, the article by Aho et al. shows that when the infection proceeds capsids can more easily traverse from the replication compartment into the chromatin, which means that infection can modify chromatin for easier capsid transport. For that reason, the article is an important reference, but it needs to be cited correctly.

We agree with the reviewer that this citation was misquoted and have corrected the citation. See lines 55 and 62-64.

3) The term heterochromatin channel at lines 54, 102, and 303 is misleading since the channels seen in the original referred paper are less dense chromatin areas. Also, this term is not used in the original paper where the phenomenon was first described. These less dense interchromatin channels were found by soft-X-ray tomography imaging and analyses, not by staining.

We thank the reviewer for pointing out this discrepancy and have amended the text to accurately describe the methods used in the appropriate citations. See lines 65, 115, and 383.

4) It is difficult to visualize chromatin using TEM microscopy. The values of peripheral chromatin thickness given in Figure 1e (5-15 nm) do not seem realistic given that the thickness of just one strand of histone-wrapped DNA is 11 nm. Why are the two values for WT different? If you can get so different values for WT, it is a bit worrisome (switching the WT results between the top and bottom parts of Fig. 1e would for example result in very different conclusions on the effect of macroH2A1 KO for the thickness of the chromatin layer).

*We agree with the reviewer that it is difficult to visualize chromatin by TEM. It is also important to note that comparisons can only be made between samples treated on the same day in the same way. Taking this into account, we chose to compare macroH2A1 KO cell stains to controls done at the same time, and the same for H3K27me3 depleted conditions compared to DMSO treated and prepare for EM at the same time. Visually, it is apparent that the staining in the macroH2A1 KO control cells is somewhat different than those of the H3K27me3 depleted control cells, which represents the inherent variability of this method. It is also true that one nucleosome is around 11nm, however, since the cells contain highly compacted chromatin with many other proteins present, this measurement is not appropriate to apply. Adding up the millions of nucleosomes that make up the chromosomes at 11nm each would result in a space much larger than the nucleus, therefore we focus on comparing between control and experimental conditions restricted to this assay as a relative qualitative comparison. Nevertheless, we agree with the reviewer that the notion of changing chromatin is difficult to quantify by EM and so we have taken an additional approach to test our hypothesis and confirm EM interpretations (discussed lines 391-393). We have utilized live capsid trafficking to visualize capsid movement in nuclei in the presence or absence of macroH2A1. The results from these new experiments are presented in new Figure 5 and EV5 and support our model. *

5) In lines 134-137 it says that "The enrichment of macroH2A1 and H3K27me3 was observed as large domains that were gained upon viral infection (Fig 2a), suggesting that the host landscape is altered upon infection. These gains were reflected in an increase in total protein levels measured by western blot (Fig 2b)." However, the protein levels of H3K27me3 do not seem to increase during infection. In other presented data as well (Figs. 2a, 2b, 2c, S2a) it is difficult to justify the statement that H3K27me3 is enriched in infection. When this is the case, the conclusion that the amount of heterochromatin increases in the infection (the quotation above and the one in line 315) is not supported. The statement in line 315 is also not specific since it is unclear what "newly formed heterochromatin increases" means.

We agree with the reviewer that our original description was misleading. We now have edited the text to clarify that there is redistribution of macroH2A1 and H3K27me3. In the revised manuscript, we have also included mass spectrometry data mined from Kulej et al. that show peptide counts that reflect increases in the heterochromatin markers described (see new Figure EV1a). Despite this quantitative measure, upon rigorous replicates of our western blots as requested by Reviewer 2, we concluded that the increases originally described are somewhat inconsistent by western blot. This discrepancy between mass spectrometry data and western blot is likely due to the non-linear nature of antibody binding and developing of western blots by the ECL enzymatic reaction. Therefore, our revised manuscript focuses on this redistribution as a reaction to infection and stress responses instead of a global increase as the original manuscript stated. See lines 174, 182, 196, 397 and Fig EV4d in main text and discussion sections.

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6) Quantitation of viral capsid location in H3K27me3-depleted cells seems somewhat arbitrary. It would have been more robust to calculate the number of capsids per unit length of the nuclear envelope with and without depletion.

We agree with the reviewer that the quantification of capsids in the H3K27me3-depleted conditions was arbitrary. In our revised manuscript, we have now repeated this quantification to accurately measure the phenotype observed, that is the chains of capsids lined up at the inner nuclear membrane. To do this, we used two measures: 1) the distance from the INM as less than 200nm and 2) the distance from other capsids as less than 300nm. Taking into account these two measures, we quantified the frequency with which multiple capsids lined up at the INM in WT and H3K27me3-depleted conditions. This is represented in the new Figure 5d. In the WT setting, we observe most often 1 single capsid at the INM, with a small fraction of 2 capsids. However, in the H3K27me3-depleted condition, we observe much greater numbers of capsids at the INM more frequently, as many as 16 at a time, leading to an average of 2-3 capsids at any single location. The source data for this figure are also provided. See lines 589 and Fig5d.

7) In lines 300-302 it says "Elegant electron microscopy work showed that HSV-1 infection induces host chromatin redistribution to the nuclear periphery2,8." However, the redistribution data in reference 8 is based on soft x-ray tomography and not on electron microscopy."

We have amended the text to accurately describe the methods used in the citations. See line 384.

8) The authors bundle together the effects of macroH2A1 removal and H3K27me3 depletion by saying that they both decrease the amount of heterochromatin at the nuclear periphery and therefore hinder capsid egress. This seems overly simplistic and macroH2A1 and H3K27me3 seem to act very differently, which is manifested in the drastic difference in nuclear capsid localization between the two cases. This difference needs to be discussed more.

We agree with the reviewer that there is a nuanced difference in the effect on nuclear egress in the absence of the two heterochromatin marks. Specifically, that macroH2A1 loss results in greater numbers of capsids dispersed throughout the nucleus, whereas depletion of H3K27me3 results in capsids reaching the INM and not escaping. To examine these differences further, we have carried out live imaging of capsid trafficking in macroH2A1 KO cells compared to control and found that capsids move much more slowly, consistent with our model, see new Figure 5h-I and EV5h-i. Conversely, H3K27me3 depletion does not prevent the capsids from reaching the INM, raising the question of whether they are successfully able to dock at the nuclear egress complex (NEC). To investigate this further, we obtained an antibody against the NEC component UL34 and probed during infection in our heterochromatin disrupted conditions. We found that UL34 levels are unchanged upon loss of macroH2A1 or depletion of H3K27me3, suggesting the levels of UL34 do not account for the decrease in titers. These data are now presented in new Figure EV3g-h. Furthermore, we have amended our model to include the two different scenarios upon loss of different types of heterochromatin (see new Figure 6) and discussion of these differences. See line 428.

Minor comments Line 45: Nuclear replicating viruses -> Nuclear-replicating viruses Line 56: is -> are Line 64: 25kDa -> 25 kDa Line 159: macroH2A1 cells -> macroH2A1 KO cells Line 289: The term gDNA is rarely used for viral DNA. Replace gDNA with viral DNA. Line 405: 8hpi -> 8 hpi Line 449: mm2 -> μm2 "Scale bar as indicated" words can be removed in the figure legends or at least should not be repeated many times within one figure legend.

We have amended the text to address these comments. See lines 52, 68, 76, 179, 334, 513, and 585.

Reviewer #1 (Significance (Required)):

These findings would appeal to a broad audience in the field of virology. Specifically, the researcher in the fields of virus-cell and virus-nucleus interactions. This manuscript analyses herpesvirus-induced structural changes in the chromatin structure and organization in the nucleus that are also likely to affect the intranuclear transport of viral capsids.

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

The manuscript "HSV-1 exploits heterochromatin for egress" describes the effects of heterochromatin at the nuclear periphery, macroH2A1 or H3K27me3 on HSV-1 replication and egress. Knocking out macroH2A1 or depleting H3K27me3 with high concentrations of tazemetostat depleted heterochromatin at the nuclear periphery, may not have affected HSV-1 protein expression and modestly inhibited the production of cell-free infectivity and HSV-1 genomes. macroH2A1 deposition was affected by infection, creating new heterochromatin domains which did not correlate directly with the levels of expression of the genes in them. The authors conclude that heterochromatin at the nuclear periphery dependent on macroH2A1 and H3K27me3 are critical for nuclear egress of HSV-1 capsids.

The experiments leading to the conclusion that HSV-1 capsids egress the nucleus through channels in the peripheral chromatin confirm previously published results (https://doi.org/10.1038/srep28844). The previously published EM micrographs show a much larger number of nuclear capsids, more consistent with the images in the classical literature, even in conditions when nuclear egress was not inhibited. Figures 1 and 4 show scarce nuclear capsids, even under the conditions when nuclear egress should be inhibited according to the model and analyses. The large enrichment in nuclear capsids in KO cells predicted by the model is not reflected in figure 4a, which shows only a modest increase in nuclear capsid density (the total number of nuclear capsids would be more informative). The number or density of nuclear capsids is not shown in H3K27 "depleted" cells. The robustness of the analyses of the number of capsids at the membrane in H3K27 "depleted" cells is unclear. For example, the analyses could be repeated with different cut offs, such as 2 or 4. If they are robust, then the conclusions will not change when the cutoff value is changed.

We appreciate the reviewer’s observation that to number of capsids we show differs from those published in the publication by Myllys et al. (Sci Rep 2016 PMID 27349677). It is important to note there are several differences between our study and that of Myllys et al. that explain the difference. First, as reviewer 1 pointed out, the Myllys et al. study used three-dimensional soft X-ray tomography combined with cryogenic fluorescence and electron microscopy to observe capsids in 3D rendered nuclei. Since our method uses only single ultrathin 50nm slices of cells, we cannot visualize the total number of capsids per nucleus, rather only per slice, which is why we have averaged slices of many nuclei to generate a statistical comparison between macroH2A1 KO or H3K27me3-depleted and control cells treated at the same time (see response to reviewer 1). Furthermore, these other methods are specialized techniques for 3D imaging that are beyond the scope of our study. Second, the Myllys et al. paper used B cells which are much smaller than HFFs, lending themselves to better tomography studies but not commonly used to study HSV-1 biology. Third, the Myllys et al. paper also used a different MOI and time point than we have. Taken together, these differences account for the disparity in visualizing capsids which is why we quantified capsid number across many images.

We agree with the reviewer that our quantification in the H3K27me3-depleted cells compared to control was somewhat arbitrary. As stated in the response to Reviewer 1 above, in our revised manuscript we have now repeated this quantification to accurately reflect the phenotype observed, that is the chains of capsids lined up at the inner nuclear membrane. To do this, we used two measures: 1) the distance from the INM as less than 200nm and 2) the distance from other capsids as less than 300nm. Taking into account these two measures, we quantified the frequency with which multiple capsids lined up at the INM in WT and H3K27me3-depleted conditions. This is represented in the new Figure 5d. In the WT setting, we observe most often 1 single capsid at the INM, with a small fraction of 2 capsids. However, in the H3K27me3-depleted condition, we observe much greater numbers of capsids at the INM more frequently, as many as 16 at a time, leading to an average of 2-3 capsids at any single location. The source data for this figure are also provided. See lines 589 and Fig 5d.

Furthermore, we have now also carried out live-imaging analysis of single capsids during infection which show the appropriate number of capsids expected when the full nucleus is visible. These results are presented in the new Figure 5 and EV5.

The quantitation of the western blots present no evidence of reproducibility and/or variability. The number of biologically independent experiments analyzed must be stated in each figure and the standard deviation must be presented. As presented, the results do not support the conclusions reached. The quality of western blots should also be improved. it is unclear why figure 2b shows viral gene expression in wild-type cells only, and not in KO or H3K27me3 depleted cells, which are only shown in the supplementary information. These blots presented in Figure S5a and S5b are difficult to evaluate as the signal is rather weak and the controls appear to indicate different loading levels. These blots do not appear to be consistent with the conclusions reached. Some blots (VP16, ICP0 in HFF) appear to indicate a delay in protein expression whereas others (VP16, ICP0 in RPE) appear to indicate earlier expression of higher levels. The claimed "depletion of H3K27me3 is not clear in in figure S5d, in which the levels appear to be highly variable in all cases, without a consistent pattern, with no evidence of reproducibility and/or variability, and using a mostly cytoplasmic protein as loading control. All western blots should be repeated to a publication level quality, the number of independent experiments must be clearly stated in each figure, and the reproducibility and/or variability must be indicated by the standard deviation.

*As reviewer 1 also pointed out, we appreciate that there is some variability with respect to the stated ‘increase’ in these heterochromatin marks during infection. As stated in response to reviewer 1, in our revised manuscript we have included a deeper analysis of these marks from global mass spectrometry that indicates an increase in total levels. Please see response to reviewer 1. *

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In the revised manuscript, we have now included mass spectrometry data mined from Kulej et al. that show peptide counts that reflect increases in the heterochromatin markers described (see new Figure EV1a). Despite this quantitative measure, upon rigorous replicates of our western blots as requested by Reviewer 2, we concluded that the increases originally described are somewhat inconsistent by western blot. This discrepancy between mass spectrometry data and western blot is likely due to the non-linear nature of antibody binding and developing of western blots by the ECL enzymatic reaction. Nevertheless, our genome-wide chromatin profiling showed consistent, reproducible, and statistically significant redistribution of macroH2A1 and H3K27me3 upon HSV-1 infection. Therefore, our revised manuscript now focuses on this redistribution as a reaction to infection and stress responses instead of a global increase as the original manuscript stated. See lines 174, 182, 196, 397 and Fig EV4b-c.

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With respect to viral protein levels, although there is slight variation in the levels of VP16 or ICP0 in RPEs compared to HFFs, we do not feel that this difference is biologically significant as several other measures of viral infection progression are unchanged (viral RNA, viral genome accumulation within infected cells). Furthermore, the significant difference in titers we observe is not explained by slight differences in ICP0 or VP16. Nevertheless, to document this variability in western blot and assuage any concern of impact infection progression, we have repeated each western blot presented in the paper three separate times and used these blots to quantify each relevant protein. Graphs of western blot quantitation can be found in each figure accompanying a western blot as follows:

Western blots:

Figures 3b-c, 4ab, EV1b, EV5a

Quantitation of western blots:

Figures 3d, 4c, EV1c, EV5b-f

• *

An enhanced analyses of the RNA-seq data, analyzing all individual genes rather than pooling them together, would provide better support to these conclusions. Then, the western blots are useful to show that the changes in mRNA result in changes in the levels of selected proteins.

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*We appreciate the reviewer’s interest in the RNA-seq data, however, we feel that reviewer has not understood the analysis we presented in the initial submission. To clarify, we calculated fold changes for individual genes and did not pool RNA-seq data anywhere in the manuscript. We show boxplots of log2 fold changes of individual genes. Boxplots enable summarization of the salient features of a distribution while still representing individual gene analysis. Here, the distribution being plotted is the log2 fold change of individual genes that intersect with macroH2A1 domains that change due to infection. As such, clusters 1-3 of macroH2A1 domains feature a loss in macroH2A1 due to infection and the boxplots show that the majority of genes are upregulated. To highlight this point further, in our revised manuscript we have included volcano plots of genes intersecting with each cluster also showing the split between the number of genes significantly upregulated and downregulated in each cluster at each time point (see new Figure EV3c). As expected from the boxplots, clusters 1-3 feature a much higher fraction of genes are significantly upregulated, whereas cluster 5 features a higher fraction of genes downregulated with concomitant increase in macroH2A1 due to infection. Taken together with the gene ontology analysis (new Figure Sd), these results support our model in which macroH2A1 is deposited in active regions to block transcription and promote heterochromatin formation. To further support these conclusions, we have also carried out analysis of 4sU-RNA data generated upon salt stress or heat shock and found that the regions defined by gain of macroH2A1 (i.e. clusters 5 and 6) also exhibit significant decreases in new transcription at just 1-2 hours after treatment. These data, which are presented in new Figure EV3b-c, strongly support our model in which macroH2A1 is deposited in genes downregulated upon stress response to generate new heterochromatin. *

Figure S1 raises some questions about the specificity of the macroH2A1 antibody used for CUT&Tag. As expected CUT&Tagging the cellular genome in the KO cells with the specific antibody results in lower signal than with the IgG control antibody. In contrast, viral DNA is CUT&Tagged as efficiently in the KO as in the WT cells, and in both cases significantly above the IgG controls. The simplest interpretation of these results is that the antibody cross-reacts with a protein that binds to HSV-1 genomes. The manuscript must experimentally address this possibility.

We agree with the reviewer that there is a possibility that antibodies cross react. However, we are confident that this is not the case in this scenario for the following reasons:

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*1 – We have carried out immunofluorescence analysis of macroH2A1 or H3K27me3 during HSV-1 infection and observe no overlap with ICP8 staining. We have included these images together with a histogram documenting the lack of overlap in the new Figure EV2f-g. *

• *

2 – CUT&Tag relies on the Tn5 transposase to insert barcodes into accessible regions of the genome. An inherent limitation of this method during viral infection is that the replicating viral genome is very dynamic and accessible, leading to easier and less specific insertion by the transposase. This is evidenced by the pattern of signal across the viral genome that is completely overlapping in the macroH2A1, H3K27me3 and IgG conditions. Snapshots of the full viral genome are now included in the new Figure EV2c-d.

• *

*Furthermore, using CUT&Tag with macroH2A1 antibody, we expect the transposition rate to be identical between WT and macroH2A1 KO conditions for the Ecoli and viral genomes. This is because we assume that the transposition in these two genomes is non-specific since there is no macroH2A1 present. Then, we expect the spike-in normalized CUT&Tag enrichment on the viral genome to be the same between WT and macroH2A1 KO conditions. Since IgG should not be affected by macroH2A1 KO, we expect the IgG enrichment to be same between WT and macroH2A1 KO conditions. Thus, non-specific background would result in higher enrichment in an apparent signal on viral genome in the macroH2A1 KO condition. *

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Combined with this expectation for background transposition and the following: 1) the distribution of the CUT&Tag signal across the viral genome is virtually identical between IgG, macroH2A1, and H3K27me3 CUT&Tag signal in WT and macroH2A1 KO cells (see new Figure EV2c-d), 2) that there is no colocalization between macroH2A1 or H3K27me3 with viral genomes by immunofluorescence (see new Figure EV2f-g), and 3) the whole genome correlation of the signals across CUT&Tag samples on the viral genome, but not the host, are virtually identical as presented in a heat map (see new Figure EV1g vs EV2e), we conclude that the viral CUT&Tag signal is noise. Therefore, any analysis of the signal on the viral genomes would not be biologically meaningful.

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Also, Figure S1 shows that the viral genome is CUT&Tag'ed with H3K27me3 antibody as efficiently in macro H2A1 WT and KO cells, and in both cases above the background signal from IgG control antibody. The authors conclude that the signal with the specific antibody "mirrors" that of the control antibody, but "mirroring" is not defined and the actual data show that there is a large increase in signal with the specific antibody. Not surprisingly, the background signal also increases, as the number of genomes increase while infection progresses. The authors conclude that "these results indicated that there was a significant background signal from the viral genome that could not be accounted for", but no evidence supporting this conclusion is presented. The data show clear signal above the background from the viral genome and that this signal is not affected by the presence or absence of macroH2A1. This section of the manuscript has to be thoroughly re-analyzed as there is clear H3K27 signal.

*We agree with the reviewer that as presented in the current manuscript it seems as though there is a real H3K27me3 signal. However, as stated in the above comment, the pattern of this signal matches that of all other conditions, including IgG, suggesting it is not a real signal, cross-reacted or otherwise, but rather an artifact of the methodology. See new Figure EV2. *

The concentration of tazemetostat used is high. Normally, concentrations of around 1µM are used in cells, and 10µM is often cytotoxic (for examplehttps://doi.org/10.1038/s41419-020-03266-3; https://doi.org/10.1158/1535-7163.MCT-16-0840). The effects on H3K27me3 presented in figure S1b appear to be normalized to mock infected treated cells. If so, they do not allow to evaluate the effectivity of the treatment. Cell viability after the four days treatment must be evaluated, the claimed "depletion" of H3K27me3 must be clearly demonstrated (the blots in figure S5 are not sufficient as presented), and levels of different histone methylations must be tested to support the claimed specificity of tazemetostat for H3K27me3 at the high concentrations used.

*While we agree with the reviewer that the cytotoxicity of any inhibitor is an important aspect to take into account, in this instance the reviewer is incorrect. The reviewer has cited papers that highlight the potential use of tazemetostat as a cancer-cell specific treatment for colorectal and B-cell cancers. In both of these cases, the primary conclusion is that tazemetostat’s cytotoxic property is largely corelated to mutation in EZH2. In fact, WT EZH2 treated cells had a more “cytostatic” response, which shows that tazemetostat is not toxic with WT EZH2 (Brach et al. Mol Cancer Ther. 2017, PMID 28835384) as is the case in our system. Furthermore, the Tan et al. study shows a non-transformed human fibroblast (CCD-18co) and embryonic colon epithelial (FHC) as “healthy controls” for their work in colorectal cancer cell lines in Figure 1D. These 2 cell lines, which are comparable to the WT HFF cells we used, show no reduction in viability at a log fold greater concentration than the 10 µM used in our paper. *

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*Nevertheless, we agree with the reviewer that cytotoxicity should be formally ruled out. In our original experiment, we recorded cell counts at the harvested mock, 4-, 8-, and 12 hpi and found no difference in the number of cells over the course of infection (see new Figure EV3e). We also used trypan blue staining as a measure of cell viability upon tazemetostat treatment and found no toxicity. These results are presented in new Figure EV3f. *

Furthermore, we agree with the reviewer that total H3 levels by western blot should be included in any comparison of H3 modification. While these were included in some figures, they were unintentionally omitted in others. In our revised manuscript we have now included these blots together with quantification of triplicate biological samples of H3K27me3 levels normalized to total H3. See new Figures 3, 4, EV1, and EV5.

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Minor comments. Reference No.27 is misquoted in lines 250-251, which state that it shows that "HSV-1 titers, but not viral replication, where reduced upon EZH2 inhibition." The reference actually shows inhibition of HSV-1 infectivity, DNA levels and mRNA for ICP4, ICP22 and ICP27. This reference uses much shorter treatments (12 h and only after infection). It also shows that inhibition of EZH2/1 up regulates expression of antiviral genes.

*We appreciate that the reviewer has pointed out a discrepancy between our results using an EZH2 inhibitor (tazemetostat) and those from reference 27 (Arbuckle et al., mBio, 2017 PMID 28811345) that requires clarification. The reviewer states that the treatments were 12 hours after infection, however, this is incorrect. In the Arbuckle et al. study, the authors used multiple different inhibitors at high doses for short treatments before infection and noted that this caused an upregulation in antiviral genes that blocked infection progression of multiple viruses including HCMV, Ad5 and ZIKA. Importantly, these genes include multiple immune signaling and interferon stimulated genes. In our study, we specifically use a much lower dose of EZH2 inhibitor, with respect to the IC50 value, and waited 3 days to ensure a steady state. In our system, any initial burst of immune response from the inhibitor would likely have subsided by the time we do our infection. Furthermore, supplemental figure EV1 from the Arbuckle et al. study states that EZH1/2 inhibitors do not affect nuclear accumulation of viral genomes and suppress HSV-1 IE expression in an MOI-independent manner (Arbuckle et al. Supplemental Figure 1). These results in fact support our conclusions that it is not any antiviral effect of inhibition of EZH2 that causes the decrease in titers that we observe. *

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To clarify, the IC50 value of the inhibitors used in the Arbuckle et al. study are 10 nmol/L (GSK126) and 4 nmol/L (GSK343). The IC50 is a measurement used to denote the amount of drug needed to inhibit a biological process by 50% and is commonly used in pharmacology to compare drug potency. In the Arbuckle et al. study, GSK126 was used at a concentration range of 15-30 µM, that is 1500-3000x more than the IC50 level as converted from nmol/L to µM, and GSK343 was used at a concentration range of 20-35 µM, that is 5000-8750x more than the IC50 level, to see changes in viral mRNA levels. The IC50 value for tazemetostat is 11 nmol/L which means that one would need to use a much higher molarity of tazemetostat, at least 28 µM which would be 2500x the IC50 value, to achieve the comparable biological changes as the inhibitors used in the Arbuckle et al. study. Thus, we are confident that the 10 µM concentration used in our study is an appropriate and non-toxic amount that would not impact antiviral responses at the dose and times that we used. As shown above and reported in multiple studies (for example: Knutson et al. Molecular Cancer Therapy 2014 PMID 24563539, Tan et al. Cell Death and Disease 2020 PMID 33311453 cited above, and Zhang et al. Neoplasia 2021 PMID 34246076, among others) the concentration of tazemetostat that we used is not toxic to the cells. Importantly, it was also reported that a global decrease in H3K27me3 by EZH2 inhibition using a 10 µM concentration of tazemetostat (here referred to by the identifier EPZ6438) did not impact HSV-1 RNA transcript accumulation measured by bulk sequencing (Gao et al. Antiviral Res 2020 PMID 32014498), consistent with our findings.

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In our revised manuscript, we have now included a discussion of these important points. See lines 409-428.

HFF are primary human cells but they are fibroblasts whereas the primary target of HSV-1 replication is epithelial cells. The wording used "they represent a common site of infection in humans" must be edited

We agree with the reviewer and have updated the text. See lines 109.

Disruption of macroH2A (1 and 2) results in general defects in nuclear architecture, not just peripheral chromatin (https://doi.org/10.1242/jcs.199216;, see also figure 1c and 5a, presenting invaginated and lobulated nuclei). The manuscript would benefit from including a broader discussion of the effects of macroH2A defects on the general nuclear architecture.

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We agree with the reviewer and our revised manuscript now includes a more in-depth discussion of the impact of macroH2A and other heterochromatin marks on nuclear structure. See lines 373-374 and 394.

The title should be edited, as "egress" in virology is commonly used to refer to the egress of virions from the cell, not to the nuclear egress of capsids. Adding the words nuclear and capsid should be sufficient to address this issue.

*We agree with the reviewer and will update the title to read “HSV-1 exploits host heterochromatin for nuclear egress”. Given that we are measuring multiple aspects of infection, we feel that adding the word ‘capsid’ is not necessary. *

It is unclear why preferential changes in expression of housekeeping genes would indicate "stress responses to infection". The rationale for this conclusion must be fully articulated and supported.

We agree with the reviewer that it may not be immediately clear as to why changes in house-keeping gene expression represent a stress response. In a recent study that we cite in our manuscript, Hennig et al. (PLOS Path 2018 PMID 29579120) demonstrate that changes in chromatin accessibility and gene transcription during HSV-1 infection resemble those that occur upon heat shock or salt stress. These results strongly support the model that global transcription changes caused upon stress (heat, salt, infection etc.) result in dramatic alterations to chromatin structure. In support of this notion, in our revised manuscript we now include analysis of these datasets based on our macroH2A1-defined clusters. Importantly, we found that the regions defined by gain of macroH2A1 (i.e. clusters 5 and 6) also exhibit significant decreases in new transcription at just 1-2 hours of exposure to salt and heat stress. These data, which are presented in new Figure EV3b-c, strongly support our model in which macroH2A1 is deposited on active genes to generate heterochromatin as a response to the stress of infection. We also discuss these results further in the revised manuscript, see lines 210-220, 233-236, and 424-426.

Statistical methods must be fully described in materials and methods and the number of biologically independent experiments must be stated in each figure.

*We agree with the reviewer and have included these details in each figure legend. *

Reviewer #2 (Significance (Required)):

The major strengths of the manuscript lie on the comprehensive analyses of the effects of knocking histone macroH2A in the nuclear architecture and chromatin organization. These analyses indicate that peripheral heterochromatin is defective in the KO. Another strength lies on the analyses of the news heterochromatin domains in HSV-1 infected cells. The relationship between the lack of correlation between the changes in gene expression and global heterochromatin domains defined by macroH2A1 with the main conclusion is less clear.

The major weakness is that the data presented do not strongly support the conclusions. Additional experiments are required to support the main conclusion that the effects in peripheral heterochromatin result in a biologically significant effect on capsid egress. The authors should also consider that the additional experimentation may not support the conclusion that macroH2A or H3K27me3 play critical roles in the nuclear egress of capsids.

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*To support our conclusions, we have carried out an entirely different set of experiments to track capsid movement. Bosse et al. PNAS 2015 PMID 26438852 and Aho et al. PLOS Path 2021 PMID 34910768 use live-imaging and single-particle tracking to characterize capsid motion relative to host chromatin. These approaches allowed the authors to discover that infection-induced chromatin modifications promote capsid translocation to the INM. They showed that 1) HSV-1 infection alters host heterochromatin such that open space is induced at heterochromatin boundaries, termed "corrals", in which viral capsids diffuse and 2) the movement of viral capsids through the host heterochromatin is the rate limiting step in HSV-1 nuclear egress. *

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To test our hypothesis that macroH2A1-dependent heterochromatin specifically is required, we collaborated with Dr. Jens Bosse to carry out these same experiments in our macroH2A1 KO and paired control cells. We tracked RFP-VP26 using spinning-disk confocal live imaging to track individual capsid movement within the nucleus. We found that capsids in cells lacking macroH2A1 traveled much shorter distances on average. This is represented graphically by the mean-square displacement (MSD) of capsid movement in macroH2A1 KO cells plateauing at ~0.4 µm2 vs 0.6 µm2 in WT cells, which represents the size of the “corral”, or space through which capsids diffuse. The average corral size in macroH2A1 KO cells is ~300 nm less than the average corral size in WT cells (two-thirds the size). These results are consistent with the finding that macroH2A1 limits chromatin plasticity both in vitro (Muthurajan et al. J Biol Chem 2011 PMID 21532035) and in cells (Kozlowski et al. EMBO Rep 2018 PMID 30177554). These data strongly support our hypothesis that macroH2A1-dependent heterochromatin is critical for the translocation of HSV-1 capsids through the host chromatin to reach the INM. Furthermore, these data support the model in which macroH2A1 allows for the increase of open space induced during infection. Loss of this open space restricts the movement of capsids in the nucleus, as quantified by our live-imaging experiments. These data are now included in the new Figure 5 and EV5 and described in lines 348-372 and 1011-1037.

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NOTE: These experiments were done in a separate lab using the same cells and MOI we used for our TEM studies. It is important to note that because this was done by live imaging where the full nucleus and cell are visible, the appropriate number of capsids is apparent.

Another major weakness is that the results of CUT&Tag of the viral genome are dismissed without proper justification. The authors conclude that the results invalidate the assays, but the results are consistent with cross-reactivity of the macroH2A1 antibody with another protein that interacts with the viral genomes and with H3K27me3 being associated with the viral genomes irrespectively of macroH2A1.

*We agree with the reviewer that as presented the viral genome reads were dismissed without thorough justification. As stated above, we are confident that the patterns we detected do not represent a biologically relevant signal but rather an artifact of the experimental set up. Furthermore, it is well known in the field that normalizing replicating viral genomes during lytic infection in any kind of chromatin profiling technique is fraught with inconsistencies as each cell may have a different copy number of viral genomes at any given time point. Therefore, we feel strongly that any analysis of the viral genome chromatin profile during a lytic replication at this point in time would require single cell sequencing which is beyond the scope of this study. We appreciate that this was not clearly presented in the original manuscript and in our revised submission we have included a full supplemental figure documenting the negative data that support our conclusions (see new Figure EV2). *

If the authors had additional data supporting the claim that these results do not reflect cross-reactivity or association with the viral genomes, these data must be presented. Without that additional data, the conclusions are not supported and these discussions must be removed from the manuscript. The authors may still opt to not analyze any association with the viral genomes, but they should not dismiss them as artifactual without actual evidence to support this claim. Previously published literature is also misquoted.

This study makes an incremental contribution to the previously published evidence showing that HSV-1 capsids egress the nucleus through channels in between the peripheral chromatin. It shows that disruption of the heterochromatin at the nuclear periphery, and the nuclear architecture in general, may have a modest effect on capsid egress. This information may be of interest mostly to a specialized audience focused on the egress of nuclear capsids.

While we agree with the reviewer on many points as stated above, we respectfully disagree that our study is merely an incremental contribution of interest only to a specialized audience focused on nuclear egress. As reviewer 2 states earlier, the strength of our study lies in the “comprehensive analyses of the effects of knocking histone macroH2A in the nuclear architecture and chromatin organization”, which would be of interest to a broad chromatin audience as well as virologists. Together with the new data presented here and a revised manuscript, we feel that our study would be of interest to a broad audience in the chromatin and virology fields as reviewers 1 and 3 also pointed out. Chromatin is generally analyzed in the context of how it might affect gene expression and the impact of chromatin on biological processes such as viral infections, and its structural role in the nucleus is not commonly considered. Here, we demonstrate an important example of the glaring effects of chromatin structure on the biological nuclear process of infection.

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

Lewis et al. reveal an unexpected role for heterochromatin formation in remodeling the nucleus to facilitate egress of the nuclear-replicating virus HSV1. By performing TEM in HSV1-infected primary human fibroblasts, the authors show that capsids accumulate at the inner nuclear membrane in regions of less densely stained heterochromatin, in agreement with studies in established cell lines. The authors go on to reveal that heterochromatin in the nuclear periphery of HSV1-infected primary fibroblasts was dependent on the histone variant macroH2A1 and is enriched with H3K27me3.CUT & Tag was used to profile macroH2A1 over time during lytic HSV1 infection and showed that both macroH2A1 and H3K27me3 were enriched over newly formed heterochromatic regions 10s-100s of Kb in length in active compartments. Remarkably, loss of macroH2A1 or H3K27me3 reduced released, cell free infection virus progeny and increased intranuclear capsid accumulation without detectably impacting the proportion of mature genome containing capsids, virus genome or protein accumulation. Their finding that newly remodeled heterochromatin forms in HSV infected cells and is a critical determinant for the association of capsids with the inner nuclear membrane is consistent with a critical role in egress.

I have only relatively minor editorial suggestions listed below to improve the manuscript:

Line 92: This subtitle should be revised to more precisely state the findings shown in the Fig 1 data. While the first part of the statement "HSV1 capsids associate with regions of less dense chromatin" is consistent with what is shown, the final phrase "...to escape the nucleus" is an interpretation of the data inferred from the static image.

We agree with the reviewer and have amended our text to more accurately describe the figure. See lines 138-139.

Line 96: I am not sure the statement that fibroblasts represent a "common" site of infection is supported by ref 15. FIbroblasts do, as indicated in ref 15, express the appropriate receptor(s) for virus entry and in culture support robust virus productive growth. However, in human tissue, infection of dermal fibroblasts appears rare, suggesting it may not be a "common" site of infection (PMCID: PMC8865408). Maybe simply revise wording to indicate fibroblasts represent "a site of infection or can be infected in tissue?".

We agree with the reviewer, as was also pointed out by reviewer 2, and have amended the text. See lines 109.

Line 126-127: As written it states that "....regions of the host genome that increase during infection", implying these genome regions are amplified (increase). I think the authors mean that infection increases binding of mH2A1 and H3K27me3 to broad regions of the host genome. Please clarify.

We agree with the reviewer that this was written ambiguously. As was pointed out by reviewers 1 and 2, the increase in these marks depends on the type of measurement. Therefore, we have modified the text in a revised manuscript to focus instead on the redistribution of these marks during infection. See line 138-139.

FIgS1, a,b,c,d: please indicate that 4,8,12 indicate hpi, correct? And indicate that in the legend M indicates Mock.

This is correct and we have updated this in the figure legend. See lines 625-627.

Line 197: "active compartments". Do the authors mean transcriptionally active compartments? Please clarify

This is correct and have clarified this in the text. See line 248.

Line 232: please replace "productive" with "infectious"

We agree with the reviewer and have amended our text. See line 295.

Line 233 - The authors conclude mH2A1 is important for egress, ruling out assembly before even bringing it up. As I read on, it is clear the authors addressed this important issue later on in the manuscript. That said, it was a bit jarring to conclude egress is important without addressing the assembly possibility at this juncture in the manuscript. One way to remedy this would be to move the Fig S6 assembly/capsid type data (lines 286-297, Fig S6) and surrounding text earlier to support the conclusion that mH2A1 did not detectably influence assembly, but is important for egress.

*We agree with the reviewer that the order of presentation makes it difficult to follow. Our revised manuscript now includes these important data within the same figure. See new Figure 5. *

Line 244: "progeny production" - it would be helpful to specify "cell free or released infectious virus progeny"

Line 248: change "produced" to released"

Line 273 replace "productive" with "infectious virus progeny released from infected cells"

Fig S5c: Was the plaque assay performed on cell free supernatants? This should be indicated.

We agree with the reviewer and have made all these changes in the text. See lines 285-287.

Reviewer #3 (Significance (Required)):

The experiments are well executed, the data are solid with appropriate statistical analysis and their analysis sufficiently rigorous, and the manuscript is clearly written. Moreover, the finding that HSV manipulates host heterochromatin marks to facilitate nuclear egress is significant and exciting. The work reveals an unexpected role for newly assembled heterochromatin in egress of nuclear replicating viruses like HSV1.