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Referee #4

Evidence, reproducibility and clarity

Summary:

The freshwater polyp Hydra possess the remarkable ability to regenerate a fully functional head within a few days after amputation, however when e.g., Notch signaling is inhibited the animals fail to regenerate the original head pattern. In the manuscript by Moneer et al. the authors aim to identify Notch responsive genes by RNA sequencing. 48 hours after Notch signaling inhibition with DAPT, 624 genes were up- and 207 genes downregulated. To identify putative direct Notch target genes the authors generated RNA-seq datasets at 3 and 6 hours after DAPT removal and propose that the expression of direct target genes is rapidly recovered within 3 hours as shown by the re-expression of HyHES. Furthermore, by performing motif enrichment analyses the authors propose that e.g., HyAlx and HySp5 could be direct Notch target genes.

Major comments:

1) It is not clear why the authors chose 48 hours as a time point for RNA sequencing. Why not 12 or 24 hours after DAPT exposure? Is the expression of HyHES or CnASH not downregulated at earlier time points? Furthermore, why did the authors use whole animals and not just the head tissue for RNA-seq to enrich the transcripts?

2) Why did the authors not perform RNA sequencing on head regenerating DAPT-treated animals? This would help to better understand the relationship between Notch and Wnt signaling especially as the authors showed in 2013 (Mündner et al) that the expression of Wnt3 is strongly affected in head regenerating DAPT-treated animals.

3) It is currently very difficult to fully evaluate the data. One single excel file with all up- and downregulated candidates should be provided (Trinity ID, fold change, False Discovery Rate, annotation etc.). I would have assumed that genes such as Wnt8 that are expressed at the base of the tentacles (Philipp et al., 2009) could be affected by DAPT. Is Wnt3 not affected at all in intact animals?

4) The silencing of Sp5 induces the formation of ectopic heads in intact and regenerating conditions and it has clearly been shown that Sp5 inhibits Wnt/β-catenin signaling. To call Sp5 a tentacle patterning gene just based on the identification of RBPJ-motifs in the Sp5 regulatory region is misleading, as it is currently not supported by experimental data. The fact that a regulatory motif is present in a promoter region does not mean that this regulatory motif is active.

5) This manuscript would be much more interesting and of greater importance if the authors would have added functional data for one or two candidate genes.

Minor comments:

1) Figure S1: Individual data points for the qPCR analysis should be shown and arrow bars added.

2) Figure 6: Scale bars are missing.

Significance

The manuscript is well written, and the presented results could be of interest for the Hydra field but they will not have a broad impact in the present state. I find it unfortunate that the authors did not use the datasets produced to better understand the complex regulatory network that is active during the patterning of the Hydra head.

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Referee #3

Evidence, reproducibility and clarity

Moneer et al. studied Notch target genes in the context of nematogenesis, i.e. the generation of stinging cells (nematocytes) from interstitial stem cells (i-cells), and in axial patterning, in the cnidarian Hydra. They used the Notch pathway inhibitor DAPT, a drug acting on presenilin, preventing the release of Notch intracellular domain (NICD). Bottger's team pioneered the usage of DAPT in Hydra back in 2007 and it has been used successfully since then in other cnidarians too. The authors first exposed Hydra polyps to DAPT for 48 hours, followed by transcriptomic analysis to identify Notch responsive genes. They then analyzed gene expression at 3 and 6 hours after removal of DAPT to identify direct and indirect Notch targets, respectively. Using a recently published Hydra single-cell atlas, the authors report that most Notch responsive genes are expressed in the nematocyte lineage, consistent with the known role of Notch signaling in hydrozoan nematogenesis. They also identify Notch targets in epithelial cells, consistent with a role of the pathway in axis patterning.

Overall, the manuscript is interesting, and the authors' conclusions are overall supported by the data. A strength of the paper is the good usage they make of a previously published Hydra single-cell transcriptome, which they do in collaboration with the Juliano lab who generated this data set. A weakness of the work is the dependence on Notch pharmacological inhibition and absence of genetic interference; the latter would provide evidence for specificity as opposed to phenotypes being a side effect of DAPT or high DMSO concentration (e.g. stress response, see specific point #6, below). The text reads well, and the figures are of good quality. Below is a list of points to be addressed.

1) On p. 4, the authors state: "We identified 831 genes that were differentially expressed in response to 48 hours of DAPT treatments". This refers to genes differentially expressed at T0. Then, they check the expression of these genes at T3 and T6. Were all differentially expressed genes at T3 and T6 included in the 831 genes identified at T0? Did the authors find differentially expressed genes at T3 and T6 which are not differentially expressed at T0?

2) p. 2, last paragraph: insert "the time points 3 and 6 hrs after DAPT removal" after "To characterize...". This is important to clarify that the analysis was done after removal rather than the addition of DAPT.

3) The authors normalized the expression of genes of interest to several housekeeping genes (RPL13, SDH, EF1α, GAPDH, and Actin) in their qPCR analysis. In Fig. S1, however, only "control" is written. Did the authors merge all results from the different housekeeping genes, or did they use only one reference gene as control (which one?) to generate the figure?

4) On Fig. 3 and the accompanying text on p 5, the black and grey clusters represent 90 and 80 genes, respectively. These 170 genes represent 25% of the total (170/666), not 20%. Clarify.

5) The figure number of Figure S2 is not indicated in the figure.

6) Can the authors confirm the DMSO concentration (1%)? I am aware this was the concentration used in their previous work, but it is nevertheless pretty high. High DMSO concentration could explain the stress response they observed.

7) Figure 1: on the right, few letters are missing.

8) Fig. 5B, remove lettering J,K,L from lower panel images.

9) Figure number is absent in Figure 9.

10) The authors completely ignore work on Notch signaling in other cnidarians. This not only impedes an evolutionary synthesis of the data but also leads to failure to discuss other functions Notch fulfills in cnidarian biology (e.g. immunity and regeneration).

Significance

The Notch pathway inhibitor, DAPT, has been widely used in work involving cnidarians. These studies have established a role for Notch in late-stage stinging cell differentiation and in tentacle morphogenesis in development and regeneration (Layden and Martindale, 2014; Marlow et al., 2012; Munder et al. 2013; Richards and Rentzsch, 2014, 2015; Gahan et al., 2017). It has also been shown that early-stage neurogenesis in hydrozoans is independent of Notch (Kasbauer et al. 2007; Gahan et al. 2017), which is different from bilaterian and anthozoan neurogenesis. What Moneer et al. did in the present study was to take these known phenotypes and put them in a cellular and molecular context. The results, showing that nematogenesis genes are Notch targets, are not surprising but novel. This work closes an existing knowledge gap and is important for the field.

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Referee #2

Evidence, reproducibility and clarity

In the manuscript by Moneer et al. Notch target genes are defined in Hydra using a classical Gamma-secretase inhibition approach. Gene expression analyses is done at different time-points via RNAseq and combined with single-cell data and ATAC-seq data. This is further elaborated with exact expression analysis and experiments studying the wash-out (recovery) of the inhibitor and again gene expression profiling. Regarding the target genes identifies several new and interesting target genes. The downstream transcription factors Pou4F3 and Pax6 are very interesting and the Wnt-pathway regulators as well. This is way more convincing than the previously described cross-talks.

My comments:

1) Introduction (page-3): Only few direct target genes of Notch-signaling have been identified so far. I don't agree. By now, there are several studies in the mammalian system using ChIPseq with anti-RBPJ and GSI-studies and dnMAML followed by RNAseq. In addition, there is also genomic fairly good data using the Drosophila-system. (On the other hand, there is still a need to identify in better defined systems). Please correct and add additional references.

2) Regarding Figure-2: How many genes are in each class? Are all the 624 genes downregulated after 48 hours of DAPT? (Part of these genes could still be direct Notch targets, possibly also harboring RBPJ binding motifs).

3) Some of the genes in the mammalian systems do not appear in presented study in Hydra: What happens the feedback regulators Dtx and NRARP? Is the Hydra Notch-gene itself regulated? What about oncogene c-myc? (I assume that c-myc exists also in Hydra (?).

4) Evolutionary conservation; (Regarding addition to Figure-9): For readers that are not so familiar with Hydra, it would be extremely helpful to have a summary-table (list) with conserved Notch target genes.

5) Suggestion: I am not a Hydra-expert, but, if possible, experiments using inducible dominant-negative Mastermind (dnMAML) would strengthen this manuscript.

Significance

This study by Moneer et al. is a nice and thoroughly done study, which will further advance our understanding of Notch target genes. This is of interest of readers in signal transduction and developmental biology.

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Referee #1

Evidence, reproducibility and clarity

Summary

The manuscript of Moneer et al describes RNAseq data on DAPT treated Hydra aiming to identify genes involved in the Notch pathway. The RNAseq data is compared with previously published Singe Cell Seq data. They proceed to perform hierarchical clustering, motif enrichment analysis of promoter regions and metagene analysis. The research provides a resource for other researchers that are interested in Notch signalling in Hydra.

Major comments

The research is very descriptive in nature. The RNAseq experiment is mostly well set up and analysed, however, the manuscript lacks subsequent experiments to confirm their findings or to determine the possible significance of the data. As a consequence, the authors are not able to draw clear conclusions from the data as most findings are only suggestive.

The manuscript aims to identify Notch dependent molecular pathways. However, the authors find a lot of indirect targets and a lot of the analyses involve these targets. In comparison, the few potential direct targets, which should be the core of the manuscript, do not receive sufficient attention. The manuscript would be much more significant if the focus would be on the direct targets and would include experiments to determine if the suggestions the current data provides can be confirmed and expanded upon.

Only two time points were used to establish which two time points were required to be able to differentiate between direct and indirect targets. This experiment requires more time points as well as several known direct and indirect targets as different targets will recover at different rates. Only then will the authors be able to determine whether they used the most appropriate time points.

A significant number of the figures relies heavily on a previously published paper from the same group. The methods section lacks a description of the statistical analysis performed.

Minor comments

The title of the manuscript is too strong for the data provided.

Although the introduction is well written, the results section lacks clarity and explanation. A concluding sentence at the end of each paragraph would aid the reader in analysing the significance of the findings. In results section 2 the authors mention the identification of 23 metagenes. A figure/table presenting this data would aid the presentation of this data. Fig 6 shows in situ hybridisation data that could potentially be interesting, however, the authors could add some more information to link this data to the Notch pathway.

In Fig S1 information about the control is lacking. Fig S3 shows alignments and phylogenetic trees but it is not clear what the function is of this figure. Some additional information explaining the relevance of the data would improve the manuscript.

In the methods section additional information regarding the set up and analysis of the qPCR is required (see MIQE guidelines). This includes further information on how the primers were tested.

Several of the figures use colour coding but some of these are not defined in the legends. Some of the figures/tables use abbreviations that are not defined. References are split between the regular reference list and a separate list in table S2. There appear to be very few recent references.

Significance

The manuscript provides a potential resource for further research. It might be relevant to researchers interested in Notch signalling and/or Hydra as a model organism/evolutionary studies. The data is mostly descriptive in nature. To date Notch signalling in Hydra has not received a lot of attention in the existing literature. The reviewer's area of expertise is Notch signalling in development. The reviewer is not familiar with Hydra as a model system.

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Reply to the reviewers

We thank all three reviewers for the very positive response to our paper. Only minor revisions were suggested which have all been incorporated.

Reviewer #1

We added missing taxonomic names and labels in Figure 6A and improved the punctuation throughout the manuscript.

Reviewer #2

As the reviewer suggested we added a schematic representation (Figure 11) depicting the two scenarios, which explain the evolution of DV patterning.

Reviewer #3

We did the small textual corrections suggested by the reviewer.

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Referee #3

Evidence, reproducibility and clarity

Summary

This manuscript continues a series of beautiful papers from Roth, Pechman, Lynch and colleagues analysing D/V patterning in a range of insects. The work started with Drosophila and has extended to other holometabolous and now hemimetabolous insect species.

This paper is in many ways one of the most remarkable of the series, for it shows that the mechanisms of D/V patterning in the cricket Gryllus are, in several striking respects, very similar to those known from Drosophila - much more so than in some of the other insects studied to date, even though Gryllus is phylogenetically the most distant from Drosophila.

Specifically, the authors present compelling data to show that the roles of Toll and dpp, as inferred from their knockdown phenotypes, are remarkably similar in Gryllus and Drosophila. This is very different from the consequences of toll and dpp knockdown in the hemipteran Oncopeltus, a species which almost certainly shares a more recent common ancestor with Drosophila.

The discussion, after summarising the results, addresses the interpretation of this surprising observation. The authors favour the hypothesis that the similarity between Drosophila and Gryllus is the result of convergence in the roles and regulation of Toll and dpp signalling, rather than an ancestral trait that has been lost to a greater or lesser extent in Oncopeltus, and in the two other insects previously studied. The argument for this interpretation is carefully made, on the basis of a thorough knowledge of the comparative embryological literature (including highly relevant recent work).

Major comments

The work depends on an analysis of candidate genes, not de novo functional searches. However, it builds on the well established understanding of the relevant genetic machinery in Drosophila, and on extensive knowledge of the genome and transcriptome of Gryllus, a dataset that has been substantially extended by new work reported in this paper, on ovary and embryonic transcriptomes. These data are sufficiently complete to give confidence that all orthologues of most of the known candidate genes have been identified, and to highlight the apparent absence from the Gryllus genome of any sog/chordin orthologue - a key dpp inhibitor widely involved in D/v patterning.

The embryology is beautifully described. The early stages of these very yolky eggs are not easy to handle, but the stainings reported here are almost all of high quality, as are the movies of live development using a nuclear GFP marked line.

The gene knockdowns appear to have been carried out carefully with due regard for the potential biases caused by sterility following parental RNAi. Phenotypes have been documented effectively by the expression of marker genes in fixed embryos, and by live imaging of development in knockdown embryos. Tables in the supplementary data show that sufficient numbers have been obtained. The work is carefully interpreted, and where inferences are less than certain, they are carefully phrased.

I find the results convincing, and therefore accept the conclusion of fundamental similarity between the roles of Toll and dpp in Drosophila and Gryllus.

Time will tell whether or not the authors favoured interpretation of these data as convergent is correct, but I certainly believe that the argument as here presented in the discussion is appropriate for publication in its current form. The abstract is, appropriately, more non-committal than the discussion itself on the interpretation of these results.

The paper is well written.

Minor points

Videos - please state orientation of the embryos, especially in videos 2 &4

Page 23 bottom "The early dorsal-to-ventral gradient of pMad (Figure 5AB) indicates that BMP signalling plays an important role ...." suggests would be better than indicates here, until functional data is considered.

Significance

The gene networks mediating patterning of the D/V body axis are related across the whole range of animals, with in particular the involvement of TGFb/dpp signalling being almost universal in this process. However, there are a great many variations on this theme. Even within the insects, the mechanisms that have been described for establishing localised TGFb and Toll signalling span the range from self organisation to effective maternal prelocalisation. This has made the GRN underlying D/V patterning a key model for studies of the evolution of gene regulatory networks.

This paper adds an interesting and important twist to the story. It is certainly not the result that any of us would have expected, based on prior published work from Oncopeltus.

If indeed it does turn out to be a case of convergence, a more detailed mechanistic analysis of that convergence will provide considerable insight into the reproducibility of evolution.

Other published work: There is no comparable work on D/V patterning in any other polyneopteran insect, to my knowledge.

Audience: Insect developmental biologists, evolutionary developmental biologists and others interested in the evolution of gene regulatory networks.

My expertise: Arthropod embryology, axial patterning, evolutionary developmental biology.

I have not reviewed in detail the presentation of the transcriptomic data and the phylogenetic analysis of gene sequences as presented in the supplementary info.

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Referee #2

Evidence, reproducibility and clarity

In this paper Pechmann and colleagues investigate the molecular mechanisms of dorso-ventral patterning in Gryllus bimaculatus. As a basis for their study they carry out thorough RNAseq analyses of various embryonic stages. Gryllus is a member of the hemimetabolous insects and therefore of interest for comparison with holometabolous insects such as Drosophila, Tribolium and Nasonia. Previous work has shown that there are significant differences in the use of Toll and Sog in establishing the dorso-ventral gradient of BMP signaling among Drosophila and Nasonia. Pechmann et al find that in Gryllus Toll has a similar role as in Drosophila and is regulated via Pipe, so far only found in Drosophila. Furthermore, they show by RNAi knockdown studies that loss of BMP signaling has little impact on the differentiation of mesoderm in Gryllus, like in Drosophila, hence, BMP signaling has largely a role in dorsal fates. Ventral fates are under direct control of the Toll gradient. Surprisingly, they also find that the key antagonist of BMP signaling and shuttle for BMPs, Sog, has been lost in Ensifera, the lineage leading to Gryllus.

This is a thorough and detailed study involving a series of functional experiments, which highlights the flexibility and evolvability of GRN of the dorso-ventral body axis formation in insects. The major finding that Gryllus is more similar to Drosophila than is Nasonia and Tribolium is interesting and even somewhat unexpected, since Drosophila is often regarded as the derived odd ball. The authors discuss two obvious explanations: the situation found in Gryllus and Drosophila reflects the ancestral condition, or, alternatively, it is the result of convergent evolution. They tend to favor the latter hypothesis. This study is an important advancement to our understanding, as it shows the constraints and the evolvability of a key patterning system to establish a body axis.

Even though the authors show nicely that Toll signaling is required to establish the BMP signaling gradient, the loss of Sog in Gryllus leaves the question unanswered how the long range BMP gradient and its shape is established. In Drosophila and vertebrates, Sog/Chordin acts both as an antagonist close to its source and as a shuttling factor, promoting BMP signaling at a distance, which is crucially important for the long range and the shape of the BMP signaling gradient. It would be desirable to test the function of other potential BMP antagonists (follistatin, gremlin, noggin) or competing BMPs (BMP3, ADAMP) in this context.

As a minor suggestion, I would recommend to summarize the findings in a synthetic picture depicting the evolutionary scenarios of the two hypotheses.

Significance:

This study is an important advancement to our understanding, as it shows the constraints and the evolvability of a key patterning system to establish a body axis.

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Referee #1

Evidence, reproducibility and clarity

Summary:

• The authors have carried out an extensive survey of dorso-ventral axis determination in the cricket Gryllus bimaculatus. They did this through analysing and knocking down key components of the two main pathways involved in D/V patterning, the toll pathway and BMP signalling. This analysis was placed in a comparative context, looking at published data on four other insect species, with the aim of contributing to our understanding of the evolution of D/V patterning.
• The authors find significant similarities between D/V patterning in Gryllus and in Drosophila - These similarities are both in the relative contributions of toll and BMP to D/V polarization and in the early ovarian activation of the toll pathway. Despite these similarities, a closer analyses of the molecular interactions uncovers some significant differences, most notably, the absence of several key modulators of BMP activity. These results lead the authors to conclude that the similarities in D/V patterning between Gryllus and Drosophila are due to convergence and not due to the conservation in Drosophila of an ancestral patterning mechanism that has been lost in almost all other lineages studied.

Major comments:

• All in all this is an excellent paper. There is a huge amount of data in here, and everything is done very meticulously and carefully. There is a good balance between mostly descriptive work (gene expression patterns, cell movements in WT embryos) and experimental work. I could find no obvious flaws with any of the results or methods, and I think the authors have made a convincing case to support their conclusions, without being too dogmatic.
• I don't see a need for any additional experiments beyond what the authors have done. They have covered all relevant aspects of D/V patterning, and make a convincing case with the data they have.

Minor comments:

The few comments I have are very minor and technical: -Missing taxonomic names (families) in Fig. 1

• Missing label in Fig. 6 Panel A.
• Punctuation could be improved. There are several instances of missing commas, and other places with unnecessary commas.

Significance:

• The manuscript represents an admirable amount of work. One can say that in a single paper, the authors have provided nearly as much information about Gryllus D/V patterning as is available for other "second-order" insect model species such as Oncopeltus or Nasonia. A such, it provides an additional major phylogenetic anchor point for understanding the evolution of early patterning.
• In terms of significance to advancing our knowledge, the data in the manuscript is, as stated above, an anchor point. It does not on its own provide any major novel insight, but fits into an ever-expanding body of comparative knowledge, whose importance is greater than the sum of its parts. Perhaps the most interesting conclusion, is indeed the one the authors have chosen as the selling-point of their paper, the fact that there is functional convergence in certain aspects of D/V patterning between two widely diverged insect species, with very different oogenesis and early development. This is again, not a major advance on its own, but an important additional piece of the comparative picture of early insect development.
• This paper will be of significant interest to the research community of comparative insect development (the community to which this reviewer belongs). It will also be of interest to those interested in examples of convergence at the functional and molecular level, to those interested in the evolution of gene families and to those interested specifically in the signalling pathways discussed (even in a non-comparative context).

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Reply to the reviewers

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

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

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

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

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

Major comments:

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

Speed:

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

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

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

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

Broad applicability:

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

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

PCA:

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

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

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

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

Other:

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

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

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

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

Minor comments:

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

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

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

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

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

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

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

We will add a GPLv3 license

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

We will make this change

• Ensure Schoenen is capitalized

We will make this change

Reviewer #1 (Significance):

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

Another manuscript from our lab1, as well as work from other labs have shown that stress causes significant degenerative changes in hippocampal astrocytes2,3. In the light of these observations, we do believe that our observation of chronic antidepressant treatment inducing structural plasticity in astrocytes is significant. Structural alterations in neurons after DMI treatment are of interest. But in our experience, we have not seen gross morphological (dendritic arborization) changes in hippocampal neurons as a result of antidepressant drug treatments. Such changes are restricted to spine morphology and axonal varicosities, which is beyond the capabilities of SMorph.

Reviewer #2 (Evidence, reproducibility and clarity):

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

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

Major comments/Questions:

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Minor Points :

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

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

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

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

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

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

Reviewer #2 (Significance):

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

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

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

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

References:

1. Virmani, G., D’almeida, P., Nandi, A. & Marathe, S. Subfield-specific Effects of Chronic Mild Unpredictable Stress on Hippocampal Astrocytes. doi:10.1101/2020.02.07.938472.

2. Czéh, B., Simon, M., Schmelting, B., Hiemke, C. & Fuchs, E. Astroglial plasticity in the hippocampus is affected by chronic psychosocial stress and concomitant fluoxetine treatment. Neuropsychopharmacology 31, 1616–1626 (2006).

3. Musholt, K. et al. Neonatal separation stress reduces glial fibrillary acidic protein- and S100beta-immunoreactive astrocytes in the rat medial precentral cortex. Dev. Neurobiol. 69, 203–211 (2009).

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Referee #2

Evidence, reproducibility and clarity

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

Major comments/Questions:

1. In the Results and/or Methods sections, the author should better describe how their approach is different from state-of-the-art approaches in terms of algorithms used and how these difference impacts on the speed and accuracy of the analysis.
2. Imaging was performed on a Zeiss LSM 880 airyscan confocal microscope. Is this method robust to other types of imaging techniques, other microscopes, variable levels of signal-to-noise? This should be tested and quantified.
3. Manual cropping of the cells with ImageJ was used. However, in the methods section, the authors mention that other machine learning tools could be used for this task. Why were these tools not implemented in this paper in order to propose a fully automated analysis approach in combination with SMorph?
4. In the methods section you state that cropped cells need to have a good contrast ratio for automated batch processing. Could you define what a good contrast ratio is and characterize the performance of your approach for different contrast ratio?
5. It is mentioned that the analysis routine can be interupted by a cell with lower contrast ratio. This is a major drawback of the approach (but I think that it could be easily improved), as such interruptions may not be= practicable for many applications that need to rely on automated processing.
6. Also, you should precise how the contrast ratio should be enhanced without modifying raw data in order to be processed with your approach. You suggest removing cells with lower contrast ratio from the analysis, but can this impact on the findings especially if some treatments impact on the detected fluorescence signal? Can you propose ways to improve the robustness of your approach to variable signal ratios?
7. In the Results section, you describe the time necessary to perform different analysis. However, giving a total time in hours is not very informative as this will likely vary a lot depending on the size of the dataset, complexity of the images, etc. You should compare the average time per image for both methods and types of analysis.
8. You state that for the number of branch point, the lower value of the measured slope when comparing SMorph and ImageJ was related to a constant overestimation of this parameter with ImageJ. How was this quantified? I think you should stress out more the comparison of both approaches with the manually annotated dataset.
9. How can you explain the differences in the 2D-projected Area, total skeleton length and convex hull between SMorph and ImageJ, which all show a slope around 0.83? Can you quantify the performance of both methods by comparing them with your manually annotated dataset?
10. In the introduction and discussion, you mention that you present a method that works on neurons, astrocytes and microglia. However, I don't see in the paper the comparison between the accuracy for all these cell types as you seem to have analyzed only the morphology of astrocytes.
11. You mention that your method is quite sensitive to variation in contrast ratio. You should quantify the contrast ratio throughout the experiments and ensure that this is not biasing the SMorph analysis for some of the treatments.

Minor Points :

1. Precise the exact inclusion and exclusion criteria for Soma detection and rephrase: "The high-intensity blobs were detected as a position of soma..." & "Boundary blobs coming from adjacent cells...".
2. Throughout the text, make sure to always refer to an analysis time per image or per cell and not only include absolute duration values without reference to the task at hand (e.g. in the discussion : SMorph took 40 second to complete the analysis... please state to which analysis you are exactly referring to and if applicable if it varies from cell to cell).
3. When you state in the discussion that "Although some methods do allow Sholl analysis without manual neurite tracing, they still work on one cell at a time", please precise if the only aspect that is missing from this type of analysis is batch processing (looping through the data) or if there is a major obstacle to automate this technique. This is important a SMorph do proceed with the analysis one cell at a time but can work in a loop/batch.

Significance

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

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

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Referee #1

Evidence, reproducibility and clarity

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

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

Major comments:

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

Speed:

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

Broad applicability:

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

PCA:

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

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

Other:

• All metrics and parameters should be expressed in physical units (e.g.," radii increasing by 3 pixels", axes in Figure 2, 3, 5, S2) so that readers can directly interpret them.
• The paper would profit from the insights provided by Bird & Cuntz (https://pubmed.ncbi.nlm.nih.gov/31167149/)

Minor comments:

• Usage of RGB images (8-bit per channel) seems hardly justifiable. Aren't you loosing dynamic range of GFAP signal?
• Please explain how MaxAbsScaler "prevents sub-optimal results"
• The fact that automated batch processing can stall on a single bad 'contrast ratio' image seems rather cumbersome to deal with
• Please add a license to https://github.com/parulsethi/SMorph/. Without it, other projects may shy away from using SMorph
• "mounted on stereotax" should be "mounted on a stereotaxis device"?
• Ensure Schoenen is capitalized

Significance:

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

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Reply to the reviewers

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

Reviewer #1 (Evidence, reproducibility and clarity)

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

1. It is assumed that the origami preparations were entirely uniform. How much variation was there? Is that supported by TIRF microscopy of origami preparations? Was the TIRF microscopy calibrated for uniformity of fluorescence (ie., shade correction)?

Our laboratory, Dong et al., has extensively characterized the origami uniformity and robustness of these exact pegboards. This paper was just posted on bioRxiv (Dong et. al, 2021). We have also cited this paper in our revised manuscript in reference to the characterization of the DNA origami (Line 117).

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

[[images cannot be shown]]

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

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

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

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

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

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

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

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

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

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

Lines 283-287 now read:

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

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

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

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

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

Reviewer #1 (Significance):

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

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Reviewer #2 (Evidence, reproducibility and clarity):

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

Using these principles, the authors study how ligand affinity, concentration and spacing influence the activation of the DNA-CARg and the engulfment of the loaded beads.

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

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

Major comments

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

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

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

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

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

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

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

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

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

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

Minor comments:

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

We have corrected this.

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

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

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

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

Reviewer #2 (Significance):

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

Referees cross-commenting

I find most of my three reviewing colleagues reasonable I also agrée to Reviewer #1 comments 2

Likewise, how much variation was there in the expression of the chimeric receptors?

Large variation in receptor numbers per cell could significantly alter the quantitative studies. Aside from the flow sorting for cells expressing two different molecules, how were cells selected for analysis?

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

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

Reviewer #3 (Evidence, reproducibility and clarity):

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

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

Reviewer #3 (Significance):

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

1.The densities of the freely mobile DNA ligands required to trigger phagocytosis is quite high. Was the length of the DNA duplexes optimized? The entire complex for both the intermediate and high affinity duplexes seems quite short, perhaps <10 nm. Might the stimulation be more efficient if a short stretch of DS DNA is added to increase the length to 12-13 nm?

The extracellular domain of the DNA-CAR (SNAP tag and ssDNA strand) are approximately 10 nm (PMID 28340336). The biotinylated ligand ssDNA is attached to the bilayer via neutravidin, resulting in a predicted 14 nm intermembrane spacing. The endogenous IgG FcR complex is 11.5 nm. Bakalar et al (PMID 29958103) tested the effect of antigen height on phagocytosis and found that the shortest intermembrane distance tested (approximately 15 nm) was the most effective. As the reviewer notes, the optimal distance between macrophage and target may be larger than our DNA-CAR. However we think the intermembrane spacing in our system is within the biologically relevant range.

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

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

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

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

[[image cannot be shown]]

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

[[image cannot be shown]]

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

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

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

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

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

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

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Additional experiments performed in revision

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

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Reviewer #3

Evidence, reproducibility and clarity

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

Significance:

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

1. The densities of the freely mobile DNA ligands required to trigger phagocytosis is quite high. Was the length of the DNA duplexes optimized? The entire complex for both the intermediate and high affinity duplexes seems quite short, perhaps <10 nm. Might the stimulation be more efficient if a short stretch of DS DNA is added to increase the length to 12-13 nm?
2. Are the origami mats generally laterally mobile on the bilayers. If so, what is the diffusion coefficient? Can one detect the mats accumulating in the initial interface between the bead and cell, particularly in cased where there is no phagocytosis? Would immobility of the mats make them more efficient at mediating phagocytosis compared to the monodispersed ligands, which I assume are highly mobile and might even be "slippery".
3. Breaking down the analysis into initiation and completion is interesting. When using the non-signalling adhesion constructs, would they get to the initiation stage or would that attachment be less extensive than the initiation phase.
4. It would be interesting to put these results in perspective of earier work on spacing with planar nanoarrays, although these can't be applied to beads. For integrin mediated adhesion there was a very distinct threshold for RGD ligand spacing that could be related to the size of some integrin-cytoskeletal linkers (PMID: 15067875). On the other hand, T cell activation seemed more continuous with changes in spacing over a wide range with no discrete threshold (PMID: 24117051, 24125583) unless the spacing was increased to allow access to CD45, in which case a more discrete threshold was generated (PMID: 29713075). The results here for phagocytosis with the very small ligands that would likely exclude CD45 seems to be more of a continuum without a discrete threshold, although high densities of ligand are needed. This issue of continuous sensing vs sharp threshold is biologically interesting so would be good assess this by as consistent standards are possible across systems.

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Referee #2

Evidence, reproducibility and clarity

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

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

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

Major comments

1. As a general comment, it is somewhat a pity that the authors did not use the endogenous FcR as a control. It would have been quite easy for the authors to place the SNAP-tag domain on the Fcg extracellular domain which would allow to do all their experiments in parallel, not only with the DNA-CAR, but also with a DNA-containing wild type receptor. Such a control would be important because, by using a CD86 transmembrane domain, the authors do not know whether the nanoscale localization of their chimeric receptors is reflecting that of the endogenous Fcg receptor.
2. An important issue that is discussed by the authors but not addressed in this manuscript is whether the different amount and spacing of the ligand is only impacting on signaling or also on the mechanical stress of the cells. Indeed, mechanical stress on the cytoskeleton arrangement could influence the engulfment process. For this, it would be very important to test that the different bead engulfment, for example, those shown in Fig. 4, is strictly dependent on signaling kinases. The authors should repeat the experiment of Fig. 4 a and b in the presence or absence of kinase inhibitors such as the Syk inhibitor R406 or the Src inhibitor PP2 to show whether the different phase of engulfment is dependent on the signaling function of these kinases. This crucial experiment is clearly missing from their study.
3. Another problem of this study is that the authors show in Fig. 1A the control DNA-CAR-adhesion but then hardly use it in their study. For example, the crucial experiments shown in Fig. 4 should be conducted in parallel with DNA-CAR-adhesion expressing macrophage cells. This study could provide another indication whether or not ITAM signaling is important for the engulfment process.
4. Another important aspect is how the concentration of the loaded origami pegboard is influencing the engulfment process. In particular, it would be interesting to show the padlocks with different spacings such as the 4T closed spacing versus 4s large spacing show a different dependency on the concentration of this padlock loading on the beads. This would be another important experiment to add to their study.

Minor comments:

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

Referees cross-commenting

I find most of my three reviewing colleagues reasonable

I also agree to Reviewer #1 comments 2

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

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

Significance:

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

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Referee #1

Evidence, reproducibility and clarity

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

1. It is assumed that the origami preparations were entirely uniform. How much variation was there? Is that supported by TIRF microscopy of origami preparations? Was the TIRF microscopy calibrated for uniformity of fluorescence (ie., shade correction)?
2. Likewise, how much variation was there in the expression of the chimeric receptors? Large variation in receptor numbers per cell could significantly alter the quantitative studies. Aside from the flow sorting for cells expressing two different molecules, how were cells selected for analysis?
3. The scale of the origami relative to the cells is difficult to discern in Figures 2C and D. Additional text would be helpful to indicate, for example, that the spots on the Fig. 2D inset indicate entire origami rather than ligand spots on individual origami particles.
4. Figure 5 legend, line 482: How was macrophage membrane visualized for these measurements?
5. line 265: "our data suggest that there may be a local density-dependent trigger for receptor phosphorylation and downstream signaling". This threshold-dependent trigger response was also indicated in the study of Zhang, et al. 2010. PNAS.
6. line 56: Rephrase, "we found that a minimum threshold of 8 ligands per cluster maximized FcgR-driven engulfment." It is difficult to picture how a minimum threshold maximizes something.
7. line 171: Rephrase, "we created... pegboards with very high-affinity DNA ligands that are predicted not to dissociate on a time scale of >7 hr". Remove "not".

Significance

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

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Reply to the reviewers

Response to all reviewers

We thank all the reviewers for carefully considering our manuscript and providing useful comments and suggestions. We agree with the general comment that testing our key findings in breast cancer cells is important. We will therefore carry out this work over the coming months and include this data in the revision. The other specific comments we address individually in the point-by-point responses below, which provides an outline of the other new experiments we plan to carry out prior to revision.

In addition to this, we would like to just highlight one general point that we only picked up when considering these responses. It is important to highlight this to all reviewers now, since we believe it adds clinical weight to our conclusions. This relates to the issue of P53, which our manuscript shows drives resistance to CDK4/6 inhibition in cells by inhibiting long-term cell cycle withdrawal following genotoxic damage.

P53 loss has been implicated in abemaciclib resistance in breast cancer patients (P53 mutation was detected in 2/18 responsive patients and 10/13 non-responsive patents (Patnaik et al., 2016)). This was recently corroborated in a larger scale study in breast cancer: the first whole exome sequencing study aimed at characterising intrinsic and acquired resistance to CDK4/6 inhibitors (Wander et al., 2020). In this recent study, P53 loss/mutation was identified in 0/18 sensitive tumours, 14/28 intrinsically resistant tumours, and 9/13 tumour with acquired resistance**. This was the most frequent single genetic change associated with resistance (58.5%), although 8 other genetic changes were also associated with resistance to differing degrees (7-27%).

Most of these other resistance events occurred in pathways known previously to help drive G1/S progression following CDK4/6 inhibition: i.e. fully predictable resistance mechanism (RB loss, CCNE2 amplification, ER loss, RAS/AKT1 activation, FGFR2/ERB22 mutation/amplification). Importantly, when the authors attempted to recapitulate these resistance event in breast cancer cell lines, they could demonstrate the expected increase in proliferation following CDK4/6 inhibition in all situation tested, except for P53 loss. This caused the authors to conclude that “loss of P53 function is not sufficient to drive CDK4/6i resistance”. This would appear to us to be an unsatisfactory explanation given the clinical data. However, the authors speculated further that: “Enrichment of TP53 mutation in resistant specimens may result from heavier pre-treatment (including chemotherapies), may be permissive for the development of other resistance-promoting alterations, or may cooperate with secondary alterations to drive CDK4/6i resistance in vivo.”

We believe that our data provide a crucial alternative explanation for these clinical findings. P53 does not affect the efficiency of a G1 arrest (fig.2), but rather it prevents the resulting genotoxic damage from inducing long-term cell cycle withdrawal (figs.2,3). Therefore, this could explain why it drives resistance in clinical disease but not in the in vitro cell growth assays employed by Wander et al. This highlights a crucial general point of our paper – important effects like this can be missed or misinterpreted until the true nature of long-term cell cycle withdrawal is appreciated.

As part of our breast cancer work at revision we will analyse this closely by comparing the effect of p53 loss on long-term cell cycle withdrawal. If the current RPE1 data holds true in breast cancer, then we believe that out study would provide a crucial explanation for these clinical findings, and in turn, these clinical data would throw weight behind our conclusion that genotoxic damage and p53 loss is a clinically important consequence of CDK4/6 inhibition in patients.

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Reviewer #1 (Evidence, reproducibility and clarity (Required)): Comments on 'CDK4/6 inhibitors induce replication stress to cause long-term cell cycle withdrawal' The rationale for this work is to understand the mechanism by which Cdk4/6 inhibitors inhibit tumour cell growth, specifically via senescence which seems to be a frequent outcome of Cdk4/6 inhibition. Although several mechanisms by which Cdk4/6 inhibition induce senescence have been proposed these have varied with the cancer cell model studied. To examine the mechanism for the cytostatic effect of cdk4/6i in therapy without potential confounding effects of different cancer cell line backgrounds, Crozier et al tackle this question in the non-transformed, immortalised diploid human cell line, RPE1. They use live cell imaging and colony formation to track the impact of G1 arrests of different lengths induced by a range of clinically relevant cdk4/6 inhibitors. They also use CRISPR-mediated removal of p53 to examine the role of p53 in the observed cell cycle responses. After noting that G1 arrest of over 2 days leads to a pronounced failure in continued cell cycle and proliferation that is associated with features of replication stress, they perform a proteomics analysis to determine the factors responsible for this. They discover that MCM complex components and some other replicative proteins are downregulated and overall suggest a mechanism whereby downregulation of these essential replication components during a prolonged G1 induce replication stress and ultimate failure of proliferation. They show the impact of cdk4/6 inhibition can be increased by combining with either aneuploidy induction (to indirectly elevate replication stress), aphidicolin (to directly elevate replication stress) or chemotherapy agents that damage DNA. Overall this is a well written and presented manuscript. Data are extremely clearly presented and described clearly within the text. Most appropriate controls were included and the work is performed to a high standard. I have a few comments about the proteomic analysis, and the link between MCM component deregulation and the induction of replication stress:

- We thank the reviewer for this careful, detailed review, and for their kind comments about our work.

**Major points:**

1. Relevance to cancer. I appreciate that examining the mechanism in a diploid line is a sensible place to start. However it remains a bit unclear precisely which aspects of this mechanism might be conserved in cancer. It could be helpful to provide evidence (if it exists) of the impact of cdk4/6 inhibition in tumour cells. For example, are catastrophic mitosis, senescence, etc observed? And is there anything further known about the relationship between tumour mutations such as p53 and clinical response to Cdk4/6i?

- It is important to point out that senescence is a common outcome of CDK4/6 inhibition in tumour cells, but exactly why tumour cells become senescent is still unclear. There have been many possible explanations proposed (see introduction), but so far, none of these implicate DNA damage. This is surprising for us, considering that DNA damage remains the best-known inducer of senescence and this is how most other broad-spectrum anti-cancer drugs induce permanent cell cycle exit. P53 loss has been associated with CDK4/6i resistance in the clinic, but this has also not previously been linked to genotoxic stress or senescence following CDK4/6 inhibition (see detailed description of this in comment to all reviewers above).** Therefore, our data could help to explain both of these key findings. However, we appreciate the importance of testing these results in breast cancer cells, therefore we will perform these experiments and include the data after revision.

Also - many of the phenotypes followed in this manuscript vary considerably with the length of G1 and the length of release. Which of these scenarios might mimic in vivo conditions?

- We see that a prolonged arrest (> 2 days) is necessary to see genotoxic effects in RPE cells. Clinically, palbociclib is administered in 3-week on/1-week off cycles, therefore this is consistent with the possibility that replication stress is induced during the off periods to cause genotoxic damage and cell cycle withdrawal.

Relating to the downregulation of MCM complex members, and the potential impact on origin licensing, how would this mechanism be manifest in cancer cells that have already deregulated gene transcription programs, and are already experiencing replication stress?

- We hypothesise that cancer cells with ongoing replication stress maybe more sensitive to the MCM downregulation caused by CDK4/6 inhibition. The rationale is that a reduction in licenced origins would impair the ability of dormant origins to fire in response to replication problems, therefore making elevated levels of replication stress less tolerable. This is consistent with the enhanced effect of CDK4/6 inhibition seen when replication stress is elevated in RPE cells. Moreover, others have shown that experimentally reducing MCM protein levels induces hypersensitivity to replication stress in transformed cell lines such as U2OS and HeLa (Ge et al., 2007; Ibarra et al., 2008). Thus, low MCM levels and reduced origin licensing can contribute to replication failure in cancer cells.

1. MCM protein levels and proposed impact on chromatin loading and origin licensing. Several MCM components are clearly reduced at the protein level. A chromatin assay (assaying fluorescence of signal remaining after pre-extraction of cytosolic proteins) suggests that MCM loading on chromatin is reduced, and this is taken to suggest a reduction in origin licensing. This is quite an indirect method - and it is difficult to conclude that the reduced chromatin bound fraction really represents a meaningful reduction in origin licensing. It would be more convincing if either positive and negative controls for this assay were included. Moreover it is not clear if this MCM reduction and proposed reduction in licensed origins would actually impact replication in an otherwise unperturbed state? Many more origins are licensed than actually fire during a normal S-phase, so it is not entirely clear that MCM levels could lead directly to replication stress here.

- Quantifying the non-extractable MCM proteins is in truth the most direct assay for origin licensing (not origin firing) available in human cells. To our knowledge, there are no reports of MCM loading by this or similar assays that are not strongly correlated with origin licensing per se. The reviewer is correct that modest reductions in MCM loading are well-tolerated in the absence of other perturbations. Specifically, Ge et al found no proliferation effects after 50% MCM loading reduction, but any further reduction introduced a proliferation delay (Ge et al., 2007). Of note, the U2OS cells used in that study also have a functional p53 response.

- Another important point that is worth emphasizing, is that many of the differentially downregulated proteins only function at replication forks (fig.4c). Therefore, we believe that the replication stress is a combined result of poor licencing and reduced levels of replication fork proteins that are needed after the origins fire. We will clarify this point in the revised manuscript.

1. Loss of MCM protein levels and chromatin loading occurs after 1 day, not 4 days, of Cdk4/6 inhibition. The current proposal (based on evidence from the live cell imaging, and the induction of hallmarks of replication stress in figures 1-3) seems to be that something occurs between 2 and 7 days of cdk4/6i to prevent cells from resuming a normal cell cycle. Thus the proteomics was performed between 2 and 7 days, and MCM proteins identified as major changed proteins between those times. However, according to Western blots and FACS profiles in Figure 4, the major reduction in MCM protein levels, and chromatin loading occurs already at 1 day of of cdk4/6i (Figure 4d,e,f). However, replication stress is not observed after this timepoint (Figure 3) - so this seems to decouple the timings of MCM reduction from induction of replication stress. How can this be reconciled?

- We agree that some of the observed changes to replisome components are quite considerable after just 1 day of arrest (some of these downregulations such as Cdc6 or phospho-Rb can be attributed to the cell cycle arrest itself - Cdc6 is unstable in G1 - but others, such MCM proteins, are not typically lost during G1). We were initially surprised by this too, considering that the phenotype clearly appears later than 1 day of arrest. It is important to state though, that the levels of almost all replisome components continue to decline as the duration of arrest is extended, eventually falling to considerably lower levels than seen after just 1 day. This is observed for MCM2, MCM3 and PCNA by western (fig.4e,e) and a large number of other replisome components by proteomics (fig.4c, 2 vs 7 days). Even MCM loading, which is 58% reduced after just 1-day arrest, is still reduced even further to just 20% of controls after 7 days (p- Our interpretation of the phenotypic data in light of this, is that replication problems become apparent when the number of licensed origins and the function of the replisome is compromised below a certain threshold; which most likely depends on cell type and, in particular, the levels of endogenous replication stress. So, in RPE cells, 1-day treatment is clearly tolerable, perhaps because there are still enough origins to complete DNA replication successfully. But, importantly, if replication stress is enhanced in these cells then 1-day of palbociclib arrest now starts to cause observable defects. This is evident in Figure 5h, where 1-day palbociclib treatment causes minimal effect on long-term growth on its own, but growth is reduced considerably when replication stress is elevated with genotoxic drugs. We interpret this to mean that the reduction in licenced origins and replisome components observed after 1 day of arrest, starts to become problematic in situations when replication stress is elevated.*

- This is actually an important point that we will highlight this at revision, because one prediction is that other cells with elevated replication stress (e.g. tumour cells with oncogene-induced replication stress) may begin to see defects after as little as 1-day palbociclib arrest.

**Minor points:**

1. All the live cell tracking figures would be even more informative if a quantification of key features (such as a cumulative frequency of S-phase entry, or a mean+SD of time in G1, S and G2) were also presented.

- We agree this will be useful, and we will include this information after revision.

1. In Figure 2D the cells released from palbociclib seem to delay longer in G1 until they start to enter S phase, compared to cells co-treated with STLC (Figure 2B). Why would this be? It is difficult to tell if other subtle effects might be present in between the +STCL and -STLC conditions, so additional graphs such as those suggested above might be informative here in particular.

- Fig.2d shows a representative experiment (50 cells) because it is difficult to interpret these individual cell cycle profiles when more than 50 cells are presented. However, we have all the data from 3 experiments (150 cells), therefore we will also calculate timings as suggested and present this information after revision.

1. Figure 4f It would be helpful to see the FACS plot for at least one of the conditions quantified in the graph as a comparison.

- These plots will be included after revision

1. MCM2 protein is not down in p53 wt, but is reduced in p53 KO cells - why is this? And why is MCM2 not impacted when the other MCM complex members are?

- We think perhaps there has been a mistake in interpreting these graphs. MCM2 is actually slightly lower in WT than KO cells at 1 days, and similar at 4 and 7 days (Fig.4d,e). MCM2 is also reduced slightly more than MCM3 (fig.4d,e) and MCM2, 3, 4, and 5 are all reduced by similar extents between 2 and 7 days palbociclib arrest (30-40% reductions; Fig.4c).

Inducing aneuploidy with reversine to elevate replication stress may result in additional aneuploidy-related stresses that confound this interpretation. For example, aneuploidy per se is known to elevate p21 and p53 levels, and chromosome mis-segregation could elevate DNA damage. For these reasons these experiments are not as compelling as the direct elevation of replication stress using aphidicolin.

- We agree that the aneuploidy experiment could have many different interpretations, and only one of these relates specifically to replication stress. This was also commented on by reviewer 3, so we feel it is best to remove this data and just keep the data on drugs that affect replication stress or DNA damage directly. We will address the effects of aneuploidy more extensively in a separate study.

**Interesting points to follow up/add more mechanism**

1. What is mechanism of protein downregulation of MCM etc? Was gene transcription impacted, or is this a question of protein stability? Depletion of one subunit can destabilise the complex leading to protein loss of the other MCM subunits, so perhaps this effect could be due to downregulation of a single MCM complex member.
2. Are these findings specific to Cdk4/6 inhibitors, or would another means or arresting cells in G1 have the same impact?

Both of these points are interesting questions and they are actually the focus of an entirely separate study that is ongoing. In particular, we are working on the mechanism(s) of MCM and replisome downregulation.

Reviewer #1 (Significance (Required)): The central question of the paper is an important one so this work would be of interest to many in the clinical and preclinical fields, and also to the cell cycle and replication stress fields.

- We thank the reviewer for this, and we agree that linking CDK4/6 inhibitors to genotoxic stress is important both for our understanding of cell cycle control and for cancer treatment. We are actually amazed that these drugs have not previously been linked to genotoxic stress, given that they appear to have broad pan-cancer activity and all other broad-spectrum anti-cancer drug work by causing genotoxic stress.

Reviewer #2 (Evidence, reproducibility and clarity (Required)): In this paper, Saurin and colleagues investigate the effects of CDK4/6 inhibitors on cell cycle arrest and re-entry. The authors report that long-term G1 arrest induced by CDK4/6i interferes with DNA replication during the next cell cycle, leading to DNA damage and mitotic catastrophe. Additionally, this compromised replication state sensitizes cells to chemotherapeutics that enhance replication stress. The major claims advanced in this paper are well-supported by the presented evidence. Well I have several questions regarding the significance (see below), I have only a few minor points regarding the methodology. 1) Regarding the down-regulation of MCM components induced by long-term palbo treatment shown in Figure 4: MCM levels are tightly regulated by cell cycle phase. I could imagine that this gene expression change may be a consequence of, for instance, 2 days CDK4/6i treatment arresting 95% of cells in G1 while 7 days of CDK4/6i treatment causes a 99.9% G1 arrest. The data in Figure 1B seems to argue against this hypothesis, but how was that data generated? Can the authors rule out a subtle change in S-phase % over 7 days in palbo? Alternately, is the down-regulation of MCM genes a consequence of cells entering senescence?

- We have performed extensive long-term movies with these cells, and we never see cells dividing or exiting G1 after the first day of palbociclib treatment. This is illustrated in fig.1b which demonstrates that 100% of FUCCI cells are in G1 (Red) at each of the timepoints. This will be clarified in the legend. In addition, MCM protein levels do not actually oscillate with cell cycle phase (Matson et al., 2017; Méndez and Stillman, 2000), although their mRNA levels certainly do (Leone et al., 1998; Whitfield et al., 2002). Furthermore, RPE and mammalian fibroblasts retain MCM proteins after 2 days of growth factor withdrawal despite transcriptional repression of their respective genes **(Cook et al., 2002; Matson et al., 2019)

- We see significant changes in MCM levels at a time when cells are still permissive to enter the cell cycle following drug release. Therefore, MCM reduction is not a consequence of senescence. Rather, we believe that it is one of the causes of cell cycle withdrawal following the subsequent S-phase.

2) For the drug studies presented in figure 5, it is important that the authors perform the appropriate statistical comparisons and analyses to demonstrate true synergy. The authors show that combining palbo and certain chemotherapies causes a greater decrease in clonogenicity than palbo alone. This may or may not be surprising (see below) - but this by itself is insufficient to support the claim that palbo "sensitizes" cells to genotoxins. If you treat cells with two poisons, in 9 out of 10 cases, you'll kill more cells than if you treat cells with one poison alone. But that could be due to totally independent effects - see, for instance, Palmer and Sorger Cell 2017. There are several well-established statistical methods for investigating drug synergy - like Loewe Additivity or Bliss Independence - and one of these methods should be used to analyze the drug-combination studies presented in Figure 5.

- This analysis will be performed at revision

Reviewer #2 (Significance (Required)): While this study is a comprehensive analysis of the effects of CDK4/6i in RPE1 cells in 2d culture, I am not convinced of its broader significance. 1) So far as I can tell, the authors do not cite any studies establishing that CDK4/6i results in a significant increase in G1-arrested cells in treated patients. What evidence is there for this claim? I am aware that this has been demonstrated in xenografts and in mouse models, but I could not find evidence for this from actual clinical studies. Here, I am reminded of the very interesting work from Beth Weaver's group on paclitaxel - Zasadil STM 2014. While it had been widely assumed that paclitaxel causes a mitotic arrest, they actually show that this drug kills tumor cells by promoting mitotic catastrophe without inducing a complete mitotic arrest. Similarly, in the absence of existing clinical data, the underlying assumption regarding the effects of CDK4/6i that motivates this paper may not be accurate. For instance, if CDK4/6i acts through the immune system (as suggested by Jean Zhao and others), then this G1 arrest phenotype could be entirely secondary to the drug's actual mechanism-of-action.

- We are very surprised by the suggestion that CDK4/6 inhibitors may not need to cause a G1 arrest in patient tumours. We appreciate that that these inhibitors effect the immune system in many different ways to combat tumourigenesis, but there is also an overwhelming amount of evidence that a G1 arrest in patient tumours is critical for the overall response. Perhaps the most striking evidence is the fact that RB loss in tumours is one of the best-characterised mechanism of resistance in breast cancer patients (Condorelli et al., 2018; Costa et al., 2020; Li et al., 2018; O'Leary et al., 2018; Wander et al., 2020). In addition, tumours types that typically achieve a poor CDK4/6i-induced G1 arrest in preclinical models, such as TNBCs, also exhibit a poor response to CDK4/6i therapy in patients. Recently a luminal androgen receptor subtype of TNBCs has been identified that responds to CDK4/6 inhibition, due to low CDK2 activity which can otherwise drive G1 progression independently of CDK4/6 in basal-like TNBCs (Asghar et al., 2017; Liu et al., 2017). This rationalises combination therapies that converge to inhibit G1 more effectively in this subtype (e.g. AR antagonist + CDK4/6 inhibition (Christenson et al., 2021)), which is akin to the oestrogen receptor and CDK4/6 combinations that have proven so successful at treating HR+ breast cancer. Many other combinations are also currently in trials based on the same premise that inhibiting upstream G1/S regulators can enhancing the response by inducing a more efficient G1 arrest (MEK, PI3K, AKT, mTOR) (Klein et al., 2018).

- In response to the specific question about clinical G1 arrest in patients, tumour samples from breast cancer patients shows a decrease in S-phase specific markers pRB and TopoIIa following abemaciclib treatment (Patnaik et al., 2016) and there is extensive evidence of a profound cell cycle arrest following CDK4/6 inhibition as judged by staining with the mitotic marker Ki67 (Hurvitz et al., 2020; Johnston et al., 2019; Ma et al., 2017; Prat et al., 2020). Whilst this does not formally prove a G1-arrest is specifical responsible for this overall cell cycle arrest, that is the implicit assumption given the known mechanism of action of CDK4/6 inhibitors in cells.

2) How relevant are RPE1 cells? Clinically, CDK4/6 inhibitors are combined with fulvestrant (which would not have an effect in RPE1), and the activity that they exhibit in breast cancer has not been matched in any other cancer types. The underlying biology of HR+ breast cancer (particularly regarding the regulation of CCND1 expression and the G1/S transition by estrogen) may not be recapitulated by other cell types. Moreover, the artificial media used in cell culture experiments may alter the regulation of the G1/S transition. I do not believe that these experiments conducted in RPE1 cells in 2d cell culture are generalizable.

- Fulvestrant/tamoxifen are effective because they enhance the efficiency of a CDK4/6i arrest by reducing Cyclin D expression to enhance Cyclin D-CDK4/6 inhibition. That convergence onto the G1/S transition is why ER antagonists enhance the CDK4/6 response. i.e. CDK activity is inhibited and CycD transcription is reduced, therefore this double hit allows breast cancer cells to arrest in G1 more efficiently than healthy tissue which is not oestrogen-responsive (this provides yet more evidence the G1 arrest in tumours is crucial for the clinical response). It is true that RPE1 cells do not respond to the oestrogen treatment, but that is not really relevant here in our opinion. We are not testing the efficiency of a G1 arrest beyond the initial characterisation in figure 1. We are mainly examining how cells respond to that G1 arrest afterwards. It could be that components of the cell culture media affect that downstream response in unanticipated ways, but we feel that is very unlikely.

- Having said that, we agree that the general point on the relevance of RPE cells is a valid one, and we will repeat key experiment in breast cancer cells. We suspect that the reason replisome components become widely downregulated during a G1 arrest will not be a specific phenomenon that is characteristic of one particular cell type. Nevertheless, it is important to validate that assumption.

3) I am confused about the effects of CDK4/6i on genotoxin sensitivity. Replogle and Amon PNAS 2020 and several citations contained therein report that CDK4/6i protects cells from DNA damage. Moreover, trilaciclib has recently received FDA approval for its ability to protect the bone marrow from cytotoxic chemotherapy! Is this a question of dose timing/intensity? The FDA approval of trilaciclib for this indication should certainly be discussed. This underscores my concern that certain findings in this paper are RPE1/tissue culture artifacts, with limited generalizability.

- The studies the reviewer refers to demonstrate that halting cell cycle progression can protect cells from genotoxic drugs that cause DNA damage during S-phase. However, we can only think that the reviewer must have missed the critical point here: The genotoxic agents in figure 5 were added after washout from CDK4/6 inhibition (we will highlight this more clearly in the revised manuscript). After drug removal, cells enter S-phase with replication competence problems (as a result of the CDK4/6 arrest) and they then experience additional problems during S-phase (as a result of the genotoxic agents included following washout). These effects synergise to enhance replication stress, a key conclusion of figure 5.

- This does is in no way support that notion that “findings in this paper are RPE1/tissue culture artefacts with limited generalizability”. Experiments in 2D tissue culture have furnished some of the most important fundamental discoveries in cancer research. It remains to be seen whether our study will cause a paradigm shift in our thinking about how CDK4/6 inhibitors work, but we believe that it may do. We appreciate that this will not become clear until our findings are followed up and validated in preclinical models and human disease, but that does not, in our opinion, make them any less valid at this stage. As stated earlier, we will confirm this is not a RPE1 cell phenomenon, but if this holds up in breast cancer cells then we believe our data will have an important impact on future preclinical and clinical work in this area.

**Referees cross-commenting** I think that we largely agree that RPE1 is not a great model for this study, and repeating certain key experiments in an ER+ BC line like MCF7 may be warranted.

- We agree that it would add value to examine our findings in BC cells, therefore we will address this point at revision by repeating key experiments in BC cells.

Additionally, I wanted to draw attention to the fact that, to my knowledge, the evidence for palbociclib inducing a G1 arrest in patients is incredibly spotty. For early-stage breast tumors where palbo is most effective, nearly all tumor cells are in G1 anyway. I think that it makes the most sense that palbo is actually working through immune modulation or through some secondary mechanism, rather than enforcing a G1 arrest. So I'm not sure about the premise of this study.

- As discussed above, there is extensive evidence that proliferation is reduced in response to CDK4/6 inhibition in patients (Hurvitz et al., 2020; Johnston et al., 2019; Ma et al., 2017; Patnaik et al., 2016; Prat et al., 2020). We agree that proliferation in patient tumours can be slower than observed in preclinical models, and there can be many reasons for this, especially within solid tumour where hypoxia is a major factor that limits proliferation. However, we do not agree that this implies that drugs that target these tumours do not act on proliferating cells. In fact, most other broad-spectrum non-targeted chemotherapies used to treat cancer also work by targeting dividing cells, and many of these are also more effective in early stage breast cancer. In addition, and as discussed extensively above, there are many studies supporting the interpretation that a G1 arrest is critical for CDK4/6i response in breast cancer patients. Considering all of these points, we strongly believe that the premise of our study – to characterise why a G1 arrest becomes irreversible – is valid and important. This point Is also made in numerous recent reviews which also highlight that this key mechanistic information is currently lacking (Goel et al., 2018; Klein et al., 2018; Knudsen and Witkiewicz, 2017; Wagner and Gil, 2020).

- We do not disagree that the immune effects are important in patients – indeed, we cited and discussed these studies in our manuscript. However, we would argue that this works together with a G1 arrest in tumour cells. The G1 arrest most likely induces a senescent response that stimulates immune engagement and tumour clearance. These multifactorial effect of CDK4/6 inhibition, on both the tumour and the immune system, are discussed at length in these reviews: (Goel et al., 2018; Klein et al., 2018; Wagner and Gil, 2020).

Reviewer #3 (Evidence, reproducibility and clarity (Required)): The authors clearly demonstrate, with appropriate techniques, that cells treated with clinically relevant CDK4/6 inhibitors lead to a cell cycle arrest, that is only partly reversible. The authors also demonstrate clearly that release from a cdk4/6i arrest leads to two phenomena: the inability to initiate S-phase, and a cell cycle exit in G2. The inability to initiate S-phase is partly dependent on p53, the cell cycle exit is fully dependent on p53. In the absence of p53, cells that are released from a CDK4/6i block frequently enter mitosis with unrepaired DNA lesions. The authors clearly demonstrate that cdk4/6 inhibition leads to down regulation of key replication genes. Combined treatment with genotoxic agents further exaggerates the phenotype of cell cycle exit upon cdk4/6 inhibition. **Specific comments:** Figure 1B: the loss of reversibility remains at approximately 50%. Does the phenotype of replication protein depletion not happen in the 50% of cells that do restart the cell cycle? it would be good if the authors could experimentally address the heterogeneity that is observed.

- This is actually a result of the fixed analysis use in fig.1B. The irreversibility is much higher than 50% after long durations of arrest, but at the 24h timepoint used in this fixed assay many cells have exited G1 but not yet had a chance to revert back into G1 from S/G2 phase. We will reinforce this point in the legend. This highlights the value of our extensive live cell assays that can fully capture cell cycle profiles, and accurately determine when cell do/don’t enter or withdraw from different stages of the cell cycle. We believe that an overreliance of fixed endpoints in previous studies may have contributed to the genotoxic effects in S-phase being missed previously: many studies show senescence after drug washout, but the cause of that senescence only becomes apparent when you observe that cells withdraw with defects after the first S-phase.

Figure 1C: the G1 state after S-phase. The read-out here is loss of the Fucci reporter geminin. Does observation reflect p53-dependent activation of the APC/C-Cdh1 prematerely? this is a known effect of persistent DNA damage in G2 cells.

- Yes, we expect that APC/C-Cdh1 activation causes geminin and cyclin degradation when cells permanently withdraw from the cell cycle from G2. This is likely caused by p53-dependent p21 activation in response to DNA replication defects, as has been shown previously in direct response to DNA damage.

Figure 2: there seem to be two distinct phenotypes when comparing p53-wt and p53-KO: the ability to initiate S-phase after CDK4/6i removal (which is largely gone in p53 KO, only slight number after 7d treatment). And cell cycle-drop-out after S-phase (this seems to be fully p53 dependent). I am not sure if a single mechanisms explains both.

- We agree that there are p53-dependent effects on speed/extent of S-phase entry and on the resulting withdrawal from G2. It may not be a single mechanism that connected these effects, although they may be related. Our manuscript mainly focusses on the DNA replication defects and cell cycle withdrawal, but in the future, it will be important to also characterise what causes the delay in cell cycle re-entry following CDK4/6 inhibition. We suspect that this could reflect differing depths of quiescence, potentially caused by p21, which would explain the p53-dependence.

Figure 3a: related to the proviso point. it is unclear if the p21 up regulation happens in G1 or G2 cells, and related to the inability of cells to initiate S-phase, or the cell cycle exit in G2.

- This is a good point, and as discussed above, we suspect both maybe related to p21. We will examine p21 levels during a G1 arrest to compare to the levels seen following release, and we will include this data after revision.

It is stated that a combined action of the p53 pathways and ATR signaling prevent mitotic entry in RPE-wt cells. However, ATR should also be able to do this in p53-KO cells. Does cdk4/6i inhibiton also down-regulation of ATR pathway components?

- We do not detect downregulation of any ATRi components in the mass spec data comparing 2 and 7 day palbociclib arrest.

Following the observation that CDK4/6i leads to replication stress, I would hypothesise that these cells would be very sensitive to agents that inhibit the response to replication stress (inhibitors of Wee1, ATR or Chk1). Yet, these agents work preferentially in p53-deficient cells, and require cell cycle progression. Sequential treatment with CDK4/6 inhibition followed by cell cycle checkpoint inhibition may help in uncovering the phenotype.

- This is a good point and we will perform experiments with ATR inhibitors after release from CDK4/6 inhibition to examine if this enhances the phenotype.

The authors increase the amount of replication stress using chemotherapeutic approaches or MPS1 inhibitors. The chemotherapeutic approaches are relevant clinically, but mechanistically it don't understand this beyond adding up treatments that lead to replication defects.

- We agree that the main value of these experiments is not to provide mechanistic insight, but rather to demonstrate that CDK4/6 inhibition can enhance the effect of current genotoxic drugs. Considering CDK4/6 inhibitors are well-tolerated, this could represent an effective way to enhance the tumour-selectivity of current genotoxic therapeutics. This has been suggested previously in a pancreatic cancer study (Salvador-Barbero et al., 2020), but the reasons given for synergy were different (DNA damage repair) and the order of drugs exposure was reversed (genotoxic before CDK4/6i). This underscores the potential importance of our new data.

- From a mechanistic point of view, these data do still suggest that CDK4/6i and genotoxic drugs converge onto the same replication stress phenotype, thereby supporting our overall conclusions. One interpretation is that a reduction in replisome levels and licenced replication origins impairs the ability of cells to overcome replication problems induced by chemotherapy drugs. Conceptualising how these drugs may synergize in this way will be important in designing new studies and trials to address this synergy more broadly.

The aneuploidy treatment is a bit weird, because it may trigger a p53 response, before the cells are released from a cdk4.6i arrest. besides, mps1 inhibition does more than just cause replication stress and is not very clinically relevant in this context.

- We agree that the aneuploidy experiment could have many different interpretations, and only one of these relates specifically to replication stress. This was also commented on by reviewer 1, so we feel it is best to remove this data and just keep the data on drugs that affect replication stress or DNA damage directly. We will address the effects of aneuploidy more extensively in a separate study.

Reviewer #3 (Significance (Required)): In their manuscript entitled: Crozier and co-workers studied the effects of CDK4/6 inhibition on cell growth. CDK4/6 inhibitors are currently used in the treatment for hormone-positive breast cancers, but their cell biological effects on tumor cells remain incompletely clear, which may hamper the further clinical development of these drugs for breast cancer or other cancers. Inhibition of CDK4/6 is known to trigger a cell cycle arrest, and it is currently unclear how this could lead to long-term tumor control. This manuscript addresses the question why cdk4/6 inhibitors cause long-term cell cycle exit.

- We thank the reviewer for this simple description of our work, which we think pitches the significance very clearly. There are currently 15 different CDK4/6 inhibitors in clinical trials, and more than 100 further trials using the 3 currently licenced inhibitors in a wide variety of tumour types and drug combinations. Although the clinical work on these drugs is huge, it is unclear how they cause long-term cell cycle arrest and we now link this to genotoxic stress for the first time. This explains clearly why this work is potentially very significant. We agree, however, that the main caveat is the need to demonstrate our findings are also applicable to breast cancer cells. But, if this is the case, we believe this would represent a paradigm shift in our understanding of how these drugs work, especially considering that genomic damage is an universal route to prolonged cell cycle exit in response to almost all other broad-spectrum anti-cancer drugs.

There are two issues that affect the significance of the findings: the authors start their manuscript with a strong translational/clinical issue, but solely use RPE1 cell lines to address this issue2. it remains unclear if their observations hold true in breast cancer models. it would be advised to repeat key findings in a hormone receptor-positive breast cancer model.

- We will examine the applicability of our findings in breast cancer cells and include this work at revision.

the effects of CDK4/6 inhibitors are observed in clinically relevant doses. however, the effects are observed upon switch-like wash out. this does not per se reflect the pharmacodynamics of more gradual increase and decrease of drug concentrations in tuner cells. by washing out the CDK4/6 inhibitors. the significant of this work would be greater if cell cycle exit with replication stress would be observed either in clinical samples or in vivo treated cancer cells.

- We agree that the significance of this work will ultimately only become fully apparent if replication stress is confirmed in clinical samples or in vivo. We envisage that our study will stimulate exactly this type of analysis in future. However, we would also add that the gradual increase/decrease in drug concentrations seen in patients is still likely to lead to switch like cell cycle re-entry given the switch-like nature of cell cycle controls at the G1/S transition. So, the timing may be different, but we would not predict that the downstream response in S-phase would be. However, whether replication stress is seen during drug-free washout periods in patients is clearly a critical future question, as we highlight in the discussion.

References

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Patnaik, A., Rosen, L.S., Tolaney, S.M., Tolcher, A.W., Goldman, J.W., Gandhi, L., Papadopoulos, K.P., Beeram, M., Rasco, D.W., Hilton, J.F., et al. (2016). Efficacy and Safety of Abemaciclib, an Inhibitor of CDK4 and CDK6, for Patients with Breast Cancer, Non-Small Cell Lung Cancer, and Other Solid Tumors. Cancer Discov 6, 740-753.

Prat, A., Saura, C., Pascual, T., Hernando, C., Muñoz, M., Paré, L., González Farré, B., Fernández, P.L., Galván, P., Chic, N., et al. (2020). Ribociclib plus letrozole versus chemotherapy for postmenopausal women with hormone receptor-positive, HER2-negative, luminal B breast cancer (CORALLEEN): an open-label, multicentre, randomised, phase 2 trial. Lancet Oncol 21, 33-43.

Salvador-Barbero, B., Álvarez-Fernández, M., Zapatero-Solana, E., El Bakkali, A., Menéndez, M.D.C., López-Casas, P.P., Di Domenico, T., Xie, T., VanArsdale, T., Shields, D.J., et al. (2020). CDK4/6 Inhibitors Impair Recovery from Cytotoxic Chemotherapy in Pancreatic Adenocarcinoma. Cancer Cell 37, 340-353.e346.

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Whitfield, M.L., Sherlock, G., Saldanha, A.J., Murray, J.I., Ball, C.A., Alexander, K.E., Matese, J.C., Perou, C.M., Hurt, M.M., Brown, P.O., et al. (2002). Identification of genes periodically expressed in the human cell cycle and their expression in tumors. Mol Biol Cell 13, 1977-2000.

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Referee #3

Evidence, reproducibility and clarity

The authors clearly demonstrate, with appropriate techniques, that cells treated with clinically relevant CDK4/6 inhibitors lead to a cell cycle arrest, that is only partly reversible.

The authors also demonstrate clearly that release from a cdk4/6i arrest leads to two phenomena: the inability to initiate S-phase, and a cell cycle exit in G2.

The inability to initiate S-phase is partly dependent on p53, the cell cycle exit is fully dependent on p53.

In the absence of p53, cells that are released from a CDK4/6i block frequently enter mitosis with unrepaired DNA lesions.

The authors clearly demonstrate that cdk4/6 inhibition leads to down regulation of key replication genes.

Combined treatment with genotoxic agents further exaggerates the phenotype of cell cycle exit upon cdk4/6 inhibition.

Specific comments:

Figure 1B: the loss of reversibility remains at approximately 50%. Does the phenotype of replication protein depletion not happen in the 50% of cells that do restart the cell cycle? it would be good if the authors could experimentally address the heterogeneity that is observed.

Figure 1C: the G1 state after S-phase. The read-out here is loss of the Fucci reporter geminin. Does observation reflect p53-dependent activation of the APC/C-Cdh1 prematerely? this is a known effect of persistent DNA damage in G2 cells.

Figure 2: there seem to be two distinct phenotypes when comparing p53-wt and p53-KO: the ability to initiate S-phase after CDK4/6i removal (which is largely gone in p53 KO, only slight number after 7d treatment). And cell cycle-drop-out after S-phase (this seems to be fully p53 dependent). I am not sure if a single mechanisms explains both.

Figure 3a: related to the proviso point. it is unclear if the p21 up regulation happens in G1 or G2 cells, and related to the inability of cells to initiate S-phase, or the cell cycle exit in G2.

It is stated that a combined action of the p53 pathways and ATR signaling prevent mitotic entry in RPE-wt cells. However, ATR should also be able to do this in p53-KO cells. Does cdk4/6i inhibiton also down-regulation of ATR pathway components?

Following the observation that CDK4/6i leads to replication stress, I would hypothesise that these cells would be very sensitive to agents that inhibit the response to replication stress (inhibitors of Wee1, ATR or Chk1). Yet, these agents work preferentially in p53-deficient cells, and require cell cycle progression. Sequential treatment with CDK4/6 inhibition followed by cell cycle checkpoint inhibition may help in uncovering the phenotype.

The authors increase the amount of replication stress using chemotherapeutic approaches or MPS1 inhibitors. The chemotherapeutic approaches are relevant clinically, but mechanistically it don't understand this beyond adding up treatments that lead to replication defects.

The aneuploidy treatment is a bit weird, because it may trigger a p53 response, before the cells are released from a cdk4.6i arrest. besides, mps1 inhibition does more than just cause replication stress and is not very clinically relevant in this context.

Significance

In their manuscript entitled: Crozier and co-workers studied the effects of CDK4/6 inhibition on cell growth. CDK4/6 inhibitors are currently used in the treatment for hormone-positive breast cancers, but their cell biological effects on tumor cells remain incompletely clear, which may hamper the further clinical development of these drugs for breast cancer or other cancers.

Inhibition of CDK4/6 is known to trigger a cell cycle arrest, and it is currently unclear how this could lead to long-term tumor control. This manuscript addresses the question why cdk4/6 inhibitors cause long-term cell cycle exit.

There are two issues that affect the significance of the findings:

-the authors start their manuscript with a strong translational/clinical issue, but solely use RPE1 cell lines to address this issue2. it remains unclear if their observations hold true in breast cancer models. it would be advised to repeat key findings in a hormone receptor-positive breast cancer model.

-the effects of CDK4/6 inhibitors are observed in clinically relevant doses. however, the effects are observed upon switch-like wash out. this does not per se reflect the pharmacodynamics of more gradual increase and decrease of drug concentrations in tuner cells. by washing out the CDK4/6 inhibitors. the significant of this work would be greater if cell cycle exit with replication stress would be observed either in clinical samples or in vivo treated cancer cells.

-the effects of CDK4/6 inhibitors are observed in clinically relevant doses. however, the effects are observed upon switch-like wash out. this does not per se reflect the pharmacodynamics of more gradual increase and decrease of drug concentrations in tuner cells. by washing out the CDK4/6 inhibitors. the significant of this work would be greater if cell cycle exit with replication stress would be observed either in clinical samples or in vivo treated cancer cells.

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Referee #2

Evidence, reproducibility and clarity

In this paper, Saurin and colleagues investigate the effects of CDK4/6 inhibitors on cell cycle arrest and re-entry. The authors report that long-term G1 arrest induced by CDK4/6i interferes with DNA replication during the next cell cycle, leading to DNA damage and mitotic catastrophe. Additionally, this compromised replication state sensitizes cells to chemotherapeutics that enhance replication stress.

The major claims advanced in this paper are well-supported by the presented evidence. Well I have several questions regarding the significance (see below), I have only a few minor points regarding the methodology.

1) Regarding the down-regulation of MCM components induced by long-term palbo treatment shown in Figure 4: MCM levels are tightly regulated by cell cycle phase. I could imagine that this gene expression change may be a consequence of, for instance, 2 days CDK4/6i treatment arresting 95% of cells in G1 while 7 days of CDK4/6i treatment causes a 99.9% G1 arrest. The data in Figure 1B seems to argue against this hypothesis, but how was that data generated? Can the authors rule out a subtle change in S-phase % over 7 days in palbo?

Alternately, is the down-regulation of MCM genes a consequence of cells entering senescence?

2) For the drug studies presented in figure 5, it is important that the authors perform the appropriate statistical comparisons and analyses to demonstrate true synergy. The authors show that combining palbo and certain chemotherapies causes a greater decrease in clonogenicity than palbo alone. This may or may not be surprising (see below) - but this by itself is insufficient to support the claim that palbo "sensitizes" cells to genotoxins. If you treat cells with two poisons, in 9 out of 10 cases, you'll kill more cells than if you treat cells with one poison alone. But that could be due to totally independent effects - see, for instance, Palmer and Sorger Cell 2017. There are several well-established statistical methods for investigating drug synergy - like Loewe Additivity or Bliss Independence - and one of these methods should be used to analyze the drug-combination studies presented in Figure 5.

Significance

While this study is a comprehensive analysis of the effects of CDK4/6i in RPE1 cells in 2d culture, I am not convinced of its broader significance.

1) So far as I can tell, the authors do not cite any studies establishing that CDK4/6i results in a significant increase in G1-arrested cells in treated patients. What evidence is there for this claim? I am aware that this has been demonstrated in xenografts and in mouse models, but I could not find evidence for this from actual clinical studies. Here, I am reminded of the very interesting work from Beth Weaver's group on paclitaxel - Zasadil STM 2014. While it had been widely assumed that paclitaxel causes a mitotic arrest, they actually show that this drug kills tumor cells by promoting mitotic catastrophe without inducing a complete mitotic arrest. Similarly, in the absence of existing clinical data, the underlying assumption regarding the effects of CDK4/6i that motivates this paper may not be accurate. For instance, if CDK4/6i acts through the immune system (as suggested by Jean Zhao and others), then this G1 arrest phenotype could be entirely secondary to the drug's actual mechanism-of-action.

2) How relevant are RPE1 cells? Clinically, CDK4/6 inhibitors are combined with fulvestrant (which would not have an effect in RPE1), and the activity that they exhibit in breast cancer has not been matched in any other cancer types. The underlying biology of HR+ breast cancer (particularly regarding the regulation of CCND1 expression and the G1/S transition by estrogen) may not be recapitulated by other cell types. Moreover, the artificial media used in cell culture experiments may alter the regulation of the G1/S transition. I do not believe that these experiments conducted in RPE1 cells in 2d cell culture are generalizable.

3) I am confused about the effects of CDK4/6i on genotoxin sensitivity. Replogle and Amon PNAS 2020 and several citations contained therein report that CDK4/6i protects cells from DNA damage. Moreover, trilaciclib has recently received FDA approval for its ability to protect the bone marrow from cytotoxic chemotherapy! Is this a question of dose timing/intensity? The FDA approval of trilaciclib for this indication should certainly be discussed. This underscores my concern that certain findings in this paper are RPE1/tissue culture artifacts, with limited generalizability.

Referees cross-commenting

I think that we largely agree that RPE1 is not a great model for this study, and repeating certain key experiments in an ER+ BC line like MCF7 may be warranted.

Additionally, I wanted to draw attention to the fact that, to my knowledge, the evidence for palbociclib inducing a G1 arrest in patients is incredibly spotty. For early-stage breast tumors where palbo is most effective, nearly all tumor cells are in G1 anyway. I think that it makes the most sense that palbo is actually working through immune modulation or through some secondary mechanism, rather than enforcing a G1 arrest. So I'm not sure about the premise of this study.

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Referee #1

Evidence, reproducibility and clarity

Comments on 'CDK4/6 inhibitors induce replication stress to cause long-term cell cycle withdrawal'

The rationale for this work is to understand the mechanism by which Cdk4/6 inhibitors inhibit tumour cell growth, specifically via senescence which seems to be a frequent outcome of Cdk4/6 inhibition. Although several mechanisms by which Cdk4/6 inhibition induce senescence have been proposed these have varied with the cancer cell model studied. To examine the mechanism for the cytostatic effect of cdk4/6i in therapy without potential confounding effects of different cancer cell line backgrounds, Crozier et al tackle this question in the non-transformed, immortalised diploid human cell line, RPE1. They use live cell imaging and colony formation to track the impact of G1 arrests of different lengths induced by a range of clinically relevant cdk4/6 inhibitors. They also use CRISPR-mediated removal of p53 to examine the role of p53 in the observed cell cycle responses. After noting that G1 arrest of over 2 days leads to a pronounced failure in continued cell cycle and proliferation that is associated with features of replication stress, they perform a proteomics analysis to determine the factors responsible for this. They discover that MCM complex components and some other replicative proteins are downregulated and overall suggest a mechanism whereby downregulation of these essential replication components during a prolonged G1 induce replication stress and ultimate failure of proliferation. They show the impact of cdk4/6 inhibition can be increased by combining with either aneuploidy induction (to indirectly elevate replication stress), aphidicolin (to directly elevate replication stress) or chemotherapy agents that damage DNA.

Overall this is a well written and presented manuscript. Data are extremely clearly presented and described clearly within the text. Most appropriate controls were included and the work is performed to a high standard. I have a few comments about the proteomic analysis, and the link between MCM component deregulation and the induction of replication stress:

Major points:

1. Relevance to cancer. I appreciate that examining the mechanism in a diploid line is a sensible place to start. However it remains a bit unclear precisely which aspects of this mechanism might be conserved in cancer. It could be helpful to provide evidence (if it exists) of the impact of cdk4/6 inhibition in tumour cells. For example, are catastrophic mitosis, senescence, etc observed? And is there anything further known about the relationship between tumour mutations such as p53 and clinical response to Cdk4/6i? Also - many of the phenotypes followed in this manuscript vary considerably with the length of G1 and the length of release. Which of these scenarios might mimic in vivo conditions? Relating to the downregulation of MCM complex members, and the potential impact on origin licensing, how would this mechanism be manifest in cancer cells that have already deregulated gene transcription programs, and are already experiencing replication stress?
2. MCM protein levels and proposed impact on chromatin loading and origin licensing. Several MCM components are clearly reduced at the protein level. A chromatin assay (assaying fluorescence of signal remaining after pre-extraction of cytosolic proteins) suggests that MCM loading on chromatin is reduced, and this is taken to suggest a reduction in origin licensing. This is quite an indirect method - and it is difficult to conclude that the reduced chromatin bound fraction really represents a meaningful reduction in origin licensing. It would be more convincing if either positive and negative controls for this assay were included. Moreover it is not clear if this MCM reduction and proposed reduction in licensed origins would actually impact replication in an otherwise unperturbed state? Many more origins are licensed than actually fire during a normal S-phase, so it is not entirely clear that MCM levels could lead directly to replication stress here.
3. Loss of MCM protein levels and chromatin loading occurs after 1 day, not 4 days, of Cdk4/6 inhibition. The current proposal (based on evidence from the live cell imaging, and the induction of hallmarks of replication stress in figures 1-3) seems to be that something occurs between 2 and 7 days of cdk4/6i to prevent cells from resuming a normal cell cycle. Thus the proteomics was performed between 2 and 7 days, and MCM proteins identified as major changed proteins between those times. However, according to Western blots and FACS profiles in Figure 4, the major reduction in MCM protein levels, and chromatin loading occurs already at 1 day of of cdk4/6i (Figure 4d,e,f). However, replication stress is not observed after this timepoint (Figure 3) - so this seems to decouple the timings of MCM reduction from induction of replication stress. How can this be reconciled?

Minor points:

1. All the live cell tracking figures would be even more informative if a quantification of key features (such as a cumulative frequency of S-phase entry, or a mean+SD of time in G1, S and G2) were also presented.
2. In Figure 2D the cells released from palbociclib seem to delay longer in G1 until they start to enter S phase, compared to cells co-treated with STLC (Figure 2B). Why would this be? It is difficult to tell if other subtle effects might be present in between the +STCL and -STLC conditions, so additional graphs such as those suggested above might be informative here in particular.
3. Figure 4f It would be helpful to see the FACS plot for at least one of the conditions quantified in the graph as a comparison.
4. MCM2 protein is not down in p53 wt, but is reduced in p53 KO cells - why is this? And why is MCM2 not impacted when the other MCM complex members are?
5. Inducing aneuploidy with reversine to elevate replication stress may result in additional aneuploidy-related stresses that confound this interpretation. For example, aneuploidy per se is known to elevate p21 and p53 levels, and chromosome mis-segregation could elevate DNA damage. For these reasons these experiments are not as compelling as the direct elevation of replication stress using aphidicolin.

Interesting points to follow up/add more mechanism

1. What is mechanism of protein downregulation of MCM etc? Was gene transcription impacted, or is this a question of protein stability? Depletion of one subunit can destabilise the complex leading to protein loss of the other MCM subunits, so perhaps this effect could be due to downregulation of a single MCM complex member.
2. Are these findings specific to Cdk4/6 inhibitors, or would another means or arresting cells in G1 have the same impact?

Significance

The central question of the paper is an important one so this work would be of interest to many in the clinical and preclinical fields, and also to the cell cycle and replication stress fields.

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Reply to the reviewers

We are grateful to the editors at Review Commons and to the reviewers for their thoughtful attention to our manuscript. Our work presents data showing that deletion of the apoptosis regulator Mcl-1 in CNS stem cells that give rise to neurons and glia resulted in specific degeneration of the white matter, beginning after postnatal day 7 (P7). Cellular analysis shows that oligodendrocytes were depleted while astrocytes persisted. Co-deletion of apoptosis effectors Bax or Bak rescued different aspects of the Mcl-1 deletion phenotype, confirming the role of apoptosis. Based on these observations, we conclude that oligodendrocytes require MCL-1 to prevent spontaneous apoptosis, and that MCL-1 depletion results in leukodystrophy, which resembles severe cases of the human disorder Vanishing White Matter Disease (VWMD). We further suggest that MCL-1 deficiency, caused by the eIF2B mutations of VWMD, may play a critical role in VWMD pathogenesis.

The reviewers questioned the similarity of the Mcl-1 deletion phenotype to VWMD and were not convinced that MCL-1 deficiency is integral to VWMD. Based on reviewer feedback, we concede that a firm link to VWMD is not supported by the available data. We consider, however, that our findings that MCL-1 is required for oligodendrocyte survival and white matter stability remain highly significant. Accordingly, we propose to revise the work as suggested by Reviewer 1 to highlight the insight our data provide as to apoptosis regulation in glia and its importance for brain development, and to revise the title, as suggested by Reviewer 3, to remove the specific reference to VWMD.

In the revision, we will make clear that the comparison to specific leukodystrophies is hypothetical and will require extensive follow-up experiments that are suggested by the findings of this work, as described in the reviews. Revising our work by removing the assertion that our data strongly implicate MCL-1 in VWMD pathogenesis will address the main reviewer concern, strengthen the logical flow, and highlight the potential for MCL-1 to be broadly relevant to white matter pathology. The significance of our findings that oligodendrocytes depend on MCL-1 protein to prevent their spontaneous apoptosis, and that MCL-1 deficiency produces white matter degeneration, will not be altered by these changes. Our data will continue to show that MCL-1 dependence is a physiologic vulnerability of oligodendrocytes that sets them apart from astrocytes and neurons and that this vulnerability is sufficient to cause white matter-specific brain degeneration when MCL-1 expression is blocked.

The other issues raised by the reviewers are all tractable and can be addressed with new experiments that we can complete in a short time-frame, such as studies of retinal pathology and addition immunohistochemistry studies, or with changes to the text. We consider that with these revisions, the manuscript will be an important contribution to understanding glial biology and the pathogenesis of white matter-specific disorders. We describe in detail below our responses to reviewer feedback and planned changes to the manuscript.

Reviewer comments are in italics and our responses are in plain text.

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

**Comments** *

While we acknowledge many important points in this review, this first point is based on a premise that is inaccurate. Based on published data, we respectfully disagree with the statement that “Depletion of MCL-1 in any tissue would promote apoptosis in cells of this tissue”. Most cells do not require an anti-apoptotic protein to prevent spontaneous apoptosis; cells that depend on anti-apoptotic proteins are specifically referred to as “primed for apoptosis” (1-5). Our conditional deletion genotypes ablated Mcl-1 in neurons of the forebrain and cerebellum and in all subtypes of glial cells. The loss of oligodendrocytes in our Mcl-1-deleted mice shows that a specific subset of white matter cells in the postnatal brain require MCL-1. Together with the increase in apoptosis and the rescues by co-deletion of Bax or Bak, these data demonstrate that cells within the oligodendrocyte lineage are primed for apoptosis in a manner that is restricted by MCL-1. In contrast, we have shown in published data that we cite in this manuscript that conditional deletion of Mcl-1 cerebellar granule neurons, the largest neuronal population in the brain, does not cause apoptosis (6); these data provide direct evidence that large populations of cells in the brain do not depend on MCL-1. We therefore disagree with the characterization of the brain-specific Mcl-1 deletion phenotype as “non-specific”.

• The white matter disease is interpreted as similar to VWM; VWM is specifically investigated and MCL-1 is found to be decreased in VWM brain tissue. The decrease is most likely nonspecific. Decrease in MCL-1 is most likely part of a general mechanism of degeneration of brain tissue or white matter. That is a different but also important conclusion. It is essential that other progressive leukodystrophies and acquired brain diseases with tissue degeneration, such as encephalitis, are investigated as well to see whether MCL-1 is also decreased in these disorders. If so, the MCL-1 decrease in white matter disease and other brain degenerative disease should be described as a final common pathway rather than specifically applicable to VWM.*

We agree that MCL-1 is likely to be a final common point in multiple disease processes that affect white matter. As described in our response to point 3 below, we are persuaded by the reviewers that the proposed similarity of the Mcl-1 deletion phenotype and VWMD is not sufficiently supported by the available evidence. We will revise the text to make clear that we consider that impaired MCL-1 is “likely part of a general mechanism of degeneration of… white matter”.

• Adding to point 2 is the fact that the pathology of the brain-specific MCL-1 knock-out mouse does not resemble the pathology of VWM at all. The central features of VWM are abnormal astrocyte morphology with astrocytes having a few stunted processes, lack of reactive astrogliosis, lack of microgliosis, increase in number of oligodendrocytes and presence of foamy oligodendrocytes. The increase in oligodendrocytes in VWM may be such that the high cellularity leads to diffusion restriction on MRI. Bergmann glia are typically ectopic, but not reduced in number. By contrast, the brain-specific MCL-1 knock-out mouse is characterized by decreased numbers of oligodendrocytes, increased numbers of microglia, reactive astrogliosis, decreased numbers of Bergmann glia and ectopic granule cells. No morphological abnormalities of oligodendrocytes and astrocytes are observed. So, histopathologically the only shared feature is preferential involvement of the brain white matter.*

We are persuaded by the reviewers that our assertion of a high degree of similarity between the Mcl-1 deletion phenotype and VWMD was not adequately supported by our available data. In the revision, we will state that a role for MCL-1 deficiency in VWMD pathogenesis is hypothetical, and that additional studies beyond the scope of this project will be needed to test this hypothesis. However, we reassert that the white matter specificity of the Mcl-1-deletion phenotype is important.

The reviewer accurately characterizes the pathology of the Mcl-1 deletion phenotype and notes “the preferential involvement of the white matter”. We consider that the preferential involvement of white matter, and of oligodendrocytes within the white matter are highly significant. We will revise the work to focus on the Mcl-1 deletion phenotype, the white matter specificity, and the potential relevance to diverse white matter-specific disease.

While we concede that more data would be needed to firmly connect MCL-1 to VWMD, we do not agree that the Mcl-1 phenotype “does not resemble the pathology of VWM at all”. There is a diversity of published observations of pathology in VWMD and not all published reports support the descriptions in the reviewer comment. This diversity of findings is highly relevant to our work. For example, while autopsy studies of humans with end stage VWMD show lack of microgliosis (7), studies of mice with a mutation known to cause VWMD in humans, that clearly recapitulate VWMD, show robust microgliosis earlier in the disease process (8). These different observations raise the possibility that microgliosis occurs during the period of active neurodegeneration or at least that in murine brain, the VWMD process activates a microglial reaction. Either interpretation would support a likeness between Mcl-1-deleted mice and VWMD mouse models. Another study of cerebellar pathology in twin human fetuses with characteristic VWMD mutations showed complete absence of Bergmann glia (9). We propose in the revision to address the reviewer’s concerns by presenting the diversity of perspectives on microglial reaction and Bergmann glial changes in VWMD, including all of the citations above.

• The clarity of the work would benefit from a different approach to introduce the study. It would help the reader to know that (1) gray matter cell specific Mcl-1 deletion in mice did not cause apoptosis and (2) apoptosis may have different effector proteins. This important information is now in the discussion. The switch to another cell type in the brain (hGFAP+ cells) would be logical and the significance of the work may improve. When approaching the topic from the field of leukodystrophies one would not necessarily think of deleting the Mcl-1 gene, especially as this gene is not associated with any known leukodystrophy and tends to associate with preneoplastic and neoplastic disease.*

We appreciate these suggestions, which we agree will enhance the logical flow and the significance, in line with our response to point 3. We will revise the Introduction as suggested.

• The authors claim that the ISR is activated in VWM, which means that eIF2α phosphorylation levels are increased, general protein synthesis is decreased and a transcription pathway is regulated by ATF4 and other factors. However, this is not what is seen in VWM. Increased eIF2α phosphorylation and reduced general protein synthesis are not observed in VWM; strikingly, the level of eIF2α phosphorylation is reduced, general protein synthesis appears at a normal rate, and only the ATF4-regulated transcriptome is continuously expressed in VWM astrocytes. *

This point is not well-settled, as published studies show that the ISR is activated in VWMD despite decreased eIF2α phosphorylation (10, 11). Published scRNA-seq studies of mice with VWMD mutations moreover, show that the ISR transcriptome is activated in oligodendrocytes, as well as neurons, endothelial cells and microglia (8). We will address this concern in the revision by citing these published reports that show both decreased eIF2α phosphorylation and lines of evidence that support ISR activation.

Fritsh et al. show that MCL-1 protein synthesis is reduced by increased eIF2α phosphorylation due to reduced translation rates at the Mcl-1 mRNA and not due to differences in Mcl-1 mRNA levels.

We agree with this interpretation of Fritsh et al, which is fully compatible with our proposed mechanism. We suggest that ISR activation in VWMD decreases translation of Mcl-1 mRNA, leading to reduced MCL-1 protein expression. MCL-1 protein is rapidly degraded and may therefore be a more sensitive detector of impaired translation than other readouts. We currently cite published work documenting altered translation in VWMD in the manuscript and in the revision will add the reference Moon et al, which is directly on point (11).

One would a priori not expect to find altered MCL-1 synthesis rates in the mildly affected VWM mouse model Eif2B5R132H/R132H.

The model does not show reduced global translation under normal conditions, but rather hypo-activity of eIF2B affects the translation of specific mRNAs (12). We will make this point clear in the revision.

Actually, ISR deregulation has not been reported in the Eif2B5R132H/R132H VWM mouse model. The authors need to rephrase this part of their study taking this information into account, when explaining their experiments and interpreting their results.

Consistent with the data that the ISR is activated in VWMD, mice show ATF4 up-regulation and other evidence of ISR activation (13) and impaired responses to physiologic stress (14, 15). In the revision, we will add these citations. To address the reviewer concerns, we will state in the revision that ISR activation is one of many potential mechanisms of reduced MCL-1 expression.

The authors now imply that their study adds mechanistic insight into the VWM field and that is not the case.

As we describe in response to point 3, we will acknowledge in the revision that the assertion that MCL-1 deficiency causes VWMD is hypothetical.

In addition, Figure 7C shows differences in actin signal rather than MCL-1 signal, suggesting that transfer of the actin protein from the gel to the blot was not optimal for the middle lanes. MCL-1 protein may thus not be reduced in these samples from Eif2B5R132H/R132H VWM mice.

We stand by our Western blot data that show that MCL-1 levels are lower in the Eif2B5R132H/R132H VWM mouse model, coincident with the onset of symptoms. The Western blot shown is a representative image that includes 3 biological replicates for each condition and of a total of 12 mice. The quantification demonstrates the reproducibility of the finding.

• Can the authors show in which cell type was apoptosis found (lines 315-316)? Their study uses the hGFAP - Cre mouse model to generate conditional Mcl-1 knock-out mice. The original paper by Zhuo et al. describing the hGFAP - promoter mouse model suggests that Mcl-1 expression is also affected in neurons and ependymal cells. The authors can investigate this further to assess which cell types (1) are sensitive to apoptosis by Mcl-1 deletion and (2) depend on Bax and Bak.*

Apoptosis may occur at different times in different cell populations, and asynchronous apoptosis can be difficult to detect at any point in time, which can complicate the suggested studies. Despite significant effort, we have not been able to co-localize any markers with dying cells in our model.

To address the question of neuronal involvement, the revised manuscript will refer to prior published studies (16-18) which show that Mcl-1 deletion affects forebrain neural progenitors. In this context, we will discuss that our Mcl-1 deletion studies show that significant neural progenitor populations survive prenatal Mcl-1 deletion and generate appropriate cortical and hippocampal architecture in Mcl-1-deleted mice at P7, prior to the onset of white matter degeneration.

To identify involved glial cells, we quantified the cells that were depleted or persisted in the Mcl-1 deleted brain. These studies identified oligodendrocytes and Bergmann glial as cell types depleted during P7-P15, when postnatal degeneration occurs in Mcl-1 deleted mice. In contrast, astrocytes persisted, indicating that astrocytes are not MCL-1-dependent. In the review, we will add new data quantifiying the immature, PDGFRA-expression subset of oligodendrocytes, which will increase the specification of which cells are depleted by Mcl-1 deletion.

We share the reviewer’s interest in the question of which subsets of Mcl-1 dependent cells are rescued by co-deletion of Bax or Bak. As known markers may not be sufficient to distinguish these subsets, we consider that scRNA-seq studies are an ideal approach to identify these subsets and their specific gene expression patterns. However, these studies are outside the scope of the present work, which establishes that specific white matter cells depend on Mcl-1.

• Heterozygous deletion of Bak greatly reduces the number of Bak-expressing cells (Fig. 3C, line, 331-333). Authors need to explain this remarkable finding. *

As we state in the text, the reduced Bak expression in the heterozygous Bak +/- mice is consistent with a gene dosage effect, which has been observed for other genes.

Please provide raw IHC data.

Our IHC data is “raw” in the sense of unaltered. We are happy to include a supplementary figure with additional low power and high-power images of BAK staining.

Co-staining with neuronal, astrocytic or oligodendrocytic markers would be insightful.

To address this point, we have successfully performed double labeling with antibodies to BAK and with antibodies to the oligodendrocyte marker SOX10 and the astrocyte marker GFAP. We will add these images to the revision. These images show that BAK+ cells include oligodendrocytes and astrocytes. The position and morphology of the BAK+ cells show that they are not neurons.

In addition, what does the Western blot signal for the BAX protein represent in Bax homozygous knock out mice (Fig. 3C)?

We will add text stating that the small residual BAX protein detected in the conditional Bax-deleted mice can be attributed to BAX expression in cells outside the Gfap lineage, including endothelial cells, vascular fibroblasts, and microglia.

Can the percentage of BAX+ cells in Mcl-1/BaxdKO corpus callosum be determined, similarly as was done for BAK? Co-staining with neuronal, astrocytic or oligodendrocytic markers would be insightful here as well. The legend of Fig. 3D does not state what staining is shown (H&E?).

We were not able to label BAX protein in individual cells using immunohistochemistry. In contrast, BAK immunohistochemistry worked well, allowing us to analyze the cellular distribution of BAK protein. We will revise the legend in 3D to state the staining is H&E.

• What explains the strong GFAP expression in processes of Mcl-1 KO astrocytes? Are these cells refractory to apoptosis or to hGFAP-driven Cre expression and recombination? Do they lack BAK or BAX or other apopotic-regulating protein? Or do specific factors compensate for the loss of MCL-1?*

As we discuss in our response to point 1 above, not all cells require MCL-1 to prevent spontaneous apoptosis. The persistence of GFAP+ astrocytes in Mcl-1-deleted mice shows that astrocytes do not require MCL-1 to maintain their survival. These data do not mean that these astrocytes are refractory to apoptosis, but rather they are not primed for apoptosis in a way that is critically restricted by MCL-1. We will add a discussion of these implications to the revision.

• Which developing symptoms do the authors refer to in line 468? Please specify and introduce appropriate references.*

We will add a description of symptoms to the revision.

• The definition of leukodystrophies given in the paper is outdated. Leukodystrophies are not invariably progressive and fatal disorders. For more recent definition of leukodystrophies see Vanderver et al., Case definition and classification of leukodystrophies and leukoencephalopathies, Mol Genet Metab 2015, and van der Knaap et al., Leukodystrophies a proposed classification system based on pathology, Acta Neuropathol 2017.*

We appreciate this advice. We will revise the Introduction accordingly and cite the recommended work.

• It is not correct that there is no specific targeted therapy clinically implemented to arrest progression of the disease in any leukodystrophy. Perhaps hematopoietic stem cell transplantation is not specific targeted, although curative if applied in time in adrenoleukodystrophy and metachromatic leukodystrophy, but certainly genetically engineered autologous hematopoietic stem cells would qualify the definition. In any case, the suggestion that no leukodystrophy is treatable is not correct.*

We appreciate this correction. We will revise the text to provide a more detailed description of treatment options while underscoring the need for mechanistic insight.

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

In this manuscript, the authors characterize the phenotype associated with brain-specific deletion of the mcl-1 gene in mice as a model for vanishing white matter-like disease in humans. Unfortunately, the gfap gene is expressed in many cell types during development which are outside of the intended cell type for this study, so functional data presented from the mutant mice is open to interpretation. The authors have not ruled out other interpretations of their results. The authors need to address major shortcomings in their data interpretation by addressing the following issues.

We appreciate that concerns related to vision and hearing in the Mcl-1 deleted mice, and address these concerns as described below.

On line 57, the authors indicate that seizures are common in leukodystrophy. This is controversial. Patients may have attacks that look like seizures, but without EEG recordings there is no way to distinguish these events from myoclonus. The authors should note this ambiguity.

We will note this ambiguity in the revision. On line 58, the authors indicate the absence of treatments for leukodystrophies. The authors should review the following articles: PMID: 7582569, 15452666 and 27882623, and moderate the text.

We will cite these papers and moderate the text as recommended

The methods section is lacking in details in several areas. For example beginning line 136, there is virtually no indication of the MRI details without going to secondary literature. The authors should provide a brief description including magnet strength, type of imaging and the general sequence, software used to collect and analyze the images.

We will include these details in the revision.

Were the brains actually harvested fresh, where mechanical stresses easily deform brain structure, prior to immersion fixation for 48h? This could be troubling despite the method being previously published.

Brains were harvested fresh and drop fixed. We have extensive experience over more than ten years in handling brain tissue from neonatal mice and subsequently analyzing MRI images and sections. These methods have allowed us to make quantitative volumetric comparisons of the 3-dimensional architecture of the developing brain using MRI in prior studies, that detected genotypic differences in brain growth without confounding fixation artefact (19). We can confirm that no mechanical stress of handling can reproduce the white matter specific changes that we see in the Mcl-1-deleted brain. We did not detect any abnormalities in control brains subjected to the same handling techniques. Beginning on line126, the authors could at least indicate the fixative details and whether the mice were perfused or tissue was immersion fixed. Compare this lack of detail with the description of lysis buffer beginning on line 158.

We will add fixation details to the revision.

Behavioral testing at young ages is rather problematic regarding data interpretation. For example, open field testing (Fig. 2B) at postnatal day 7, which relies on visual cues, is rather dubious when mice do not open their eyes until 12-13 days after birth. How would the pups know if they were in the middle of an open field and exhibit thigmotaxis, even if they were capable of the behavior at such a young age? Thus, the P7 data likely cannot be interpreted in terms of the knockouts being normal.

We fully agree with the reviewer on the challenges with behavioral analysis of such young mice. The rationale for the open field test was that, at P7, mouse pups are gaining greater control of hind limb function, which can be observed as a transition from pivoting in one place to forward locomotion. Thus, we measured the number of pivots and distance traveled in the open field as indicators for maturation of motor function. Center time was presented to show that, at P7, both WT and knockout mice stayed in the middle (i.e., the groups were at the same stage of limited mobility). We consider that these measures, together with geotaxis and latency to righting (Table 1), provide a developmentally-appropriate neurologic assessment for an age when behaviors are very limited. We will make clear in the revision that these specific tests must be considered together in order to be informative.

By P14, when the mutants exhibit a phenotype, they are already significantly underweight, which can lead to non-specific phenotypes such as retinal dysfunction or degeneration. Did the authors look for pathological changes in the retina?

Further, GFAP is expressed in retina of many vertebrate species (PMID 1283834) which would inactivate mcl1 in that tissue and possibly lead to blindness. Indeed, the table at the following link provides a list of tissues in which the gfap-cre transgene is expressed during development. The authors need to address this major issue. http://www.informatics.jax.org/allele/MGI:2179048?recomRibbon=open

We appreciate this suggestion and we will look for pathology in the retina and optic nerve. Such pathology, if we find it, is likely to be specific, as the optic nerve is myelinated and we have already noted extensive myelination abnormalities in the Mcl-1-deleted mice. If we find retinal or optic nerve abnormalities, we will note the potential for these abnormalities to impact on open field testing.

For the startle response, which relies on normal hearing, did the authors check to determine if the mutants are deaf? This is very difficult at such a young age, especially prior to tight junction assembly in the lateral wall at around P14. Again, GFAP is expressed in the cochlea at an early age (see PMID 20817025) and may have caused degenerative pathology in this tissue. The authors need to address this major issue.

The reviewer brings up the potential issue of deafness as a confounding factor for acoustic startle testing. Our results showed that startle responses in the mutant mice were increased at P14, which clearly indicates the mice were able to hear the acoustic stimuli. Further, at P14 and P21, both WT and knockout mice had orderly patterns of prepulse inhibition, providing confirmation of good hearing ability at each timepoint. We will make these points clear in the revision.

*Reviewer #2 (Significance (Required)):

Unknown.*

The reviewer has not raised specific issues with the significance. We consider the significance of our work to be the finding that oligodendrocyte-lineage glial cells depend on MCL-1 and thus are primed for apoptosis, such that disrupting MCL-1 expression results in catastrophic degeneration of the cerebral white matter. Addressing the reviewer’s concerns described in the section on Evidence, reproducibility and clarity will support this significance.*

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

Cleveland et al. tried to argue that brain-specific depletion of apoptosis regulator MCL-1 reproduces Vanishing White Matter Disease (VWMD) in mice. The authors show that brain-specific MCL-1 deficiency leads to brain atrophy, increased brain cell apoptosis, decreased oligodendrocytes, decreased MBP immunoreactivity, and activation of astrocytes and microglia. It is known that VWMD is a hypomyelinating disorder caused by mutation of eIF2B subunits, which displays severe myelin loss but minimal oligodendrocyte apoptosis or loss in the CNS white matter. In fact, a number of studies show increased oligodendrocyte numbers in the CNS white matter.*

Published reports show decreased normal oligodendrocytes and increased immature oligodendrocyte populations (20)**.

The characteristic oligodendrocyte pathology is foamy oligodendrocytes (Wong et al., 2000), rather than apoptosis.

Foamy oligodendrocyte pathology and increased oligodendrocyte apoptosis are not mutually exclusive. The above referenced paper, Wong et al, in addition to foamy oligodendrocytes, also describes a “decrease in numbers of cells with oligodendroglial phenotype, both normal and abnormal” (21); this decrease is compatible with increased apoptosis. Moreover, published reports specifically describe apoptotic oligodendrocytes in human brains with VWMD (22). To address this point, we propose to include both of these citations in the revision to reference foamy oligodendrocyte pathology in VWMD and to state that this pathologic finding does exclude a role for apoptosis in VWMD pathogenesis.

Since the CNS pathology of brain-specific MCL-1 deficient mice is drive by brain cell apoptosis, the relevance of this mouse model to VWMD is very limited.

Whether apoptosis plays a mechanistic role in VWMD is less clear than this comment suggests, as described in multiple publications (22, 23).

The title of this manuscript is misleading, and should be changed.

We accept that our statement that Mcl-1-deletion recapitulates VWMD is premature and not adequately supported by the available data. We will revise the title, introduction and discussion accordingly, to focus on the white matter specificity of the Mcl-1-deletion phenotype.

*Moreover, there are a number of major concerns.**

1. Figure 1 clearly shows severe atrophy of neocortex in Mcl-1 cKO mice; however, the white matter appears largely normal in the cerebellum and brain stem. Mcl-1 cKO mice also display ventricular dilation and possible atrophy of corpus callosum. The authors should discuss severe atrophy of neocortex in Mcl-1 cKO mice and the possibility that ventricular dilation and corpus callosum atrophy result from severe atrophy of neocortex?*

The cortical atrophy that the reviewer notes begins after P7 and is minimal at P14 when white matter loss is already pronounced. At P21, when there is clear cortical thinning, the white matter loss is extreme. Based on the time course, we consider that the white matter loss is the primary pathology, and the cortical thinning is secondary. Importantly, glial cells populate the cortex as well as the white matter and our cellular data show that oligodendrocytes are reduced in the cortex as well as in the white matter structures. Based on these lines of evidence, we consider that the primary cell type affected is the oligodendroglial population of the glia. We will add a discussion along these lines to the revision.

We agree that the brain stem is preserved. Our data show that the hGFAP-Cre promoter is least efficient in the brain stem and midbrain regions (Sup Fig.1). We will note this differential efficiency in the revision.

• The motor and sensory tests in Figure 2 are potential interesting, but their relevance to myelin abnormalities is limited. The authors should perform the behaviors tests that are highly relevant to myelin abnormalities.*

The tests presented show progressive neurologic impairment, correlating with the onset of neuropathology. In the revision we will note that ataxia and tremor are common features of leukodystrophies and the Mcl-1-deleted mice show both ataxia and tremor.

• It is well expected that there are increased apoptotic cells in the brain of Mcl-1 cKO mice. The authors should perform double labeling to demonstrate which cell types undergo apoptosis: neurons, oligodendrocytes, or other cell types? On the other hand, Figure 3A shows that there are substantial apoptotic cells in the cerebral cortex, which is consistent with severe cerebral cortex atrophy in Mcl-1 cKO mice, suggesting neuron apoptosis in the cerebral cortex. Neuron apoptosis would further rule out the relevance of Mcl-1 cKO mice to VWMD.*

These studies would be of interest, but we have not been able to co-label apoptotic cells in the Mcl-1-deleted mice with any marker. In the advanced state of apoptosis when dying cells are detectable by TUNEL staining, the relevant marker proteins have been degraded beyond recognition by IHC. In contrast, the apoptotic marker cleaved caspase-3, which is positive earlier in the apoptotic process and might allow marker co-labeling, was not detectably elevated in the Mcl-1-deleted mice. We attribute the lack of cleaved caspase-3+ cells to the asynchronous nature of the increased cell death, and to the short duration in which dying cells are cleaved caspase-3+. While double label studies of dying cells have been problematic, our studies quantifying each cell type provide information to address the reviewer’s question. Our cell counts show clearly that oligodendrocytes are the primary cell type reduced in number in the Mcl-1 deleted mice.

• Figure1, 4 the authors use H&E staining to demonstrate white matter loss. H&E staining is good to show general CNS morphology; however, it is impossible to use H&E staining to quantify the integrity of the white matter. The authors should perform specific staining to quantify white matter loss in the mouse models.*

Our MBP stains later in the paper are used to quantify white matter loss.

• Figure 5, MBP IHC is good to show general myelin staining, but is not a reliable assay to quantify myelin integrity in the CNS. The authors should perform electron microscopy analysis to quantify myelin integrity in the CNS in the mouse models.*

Our studies of MBP staining show that the myelinated area in cross sections is significantly reduced in the Mcl-1-deleted mice. Electron microscopy studies cannot show whether the myelinated area is reduced and studies of myelin integrity are not needed to prove that reduced oligodendrocytes correlate with reduced myelination.

• Figure 6, SOX10 is a marker of oligodendrocytes and OPCs. The authors should quantify the number of oligodendrocytes (using oligodendrocyte markers, such as CC1) and the number of OPCs (using OPC markers, such as NG2). Does deletion of BAK or BAX reduce oligodendrocyte apoptosis in the CNS of Mcl-1 cKO mice?*

We agree that this is an important question, and we are working to quantify OPCs in the Mcl-1-deleted mice by counting cells labelled with the OPC marker PDGFRA. We will add these data to the revision and discuss their significance when we know what they show.

• The authors show that the level of MCL-1 is comparable in brain lysates of wildtype and eIF2B5 R132H/R132H mice at the age of 7 months, and moderately decreased in eIF2B5 R132H/R132H mice at the age of 10 months. VWMDis a developmental disorder. Similarly, brain-specific MCL-1 deficiency causes developmental abnormalities in the CNS. The normal level of MCL-1 in 7-month-old eIF2B5 R132H/R132H mice strongly suggests that MCL-1 is not a major player involved in the pathogenesis of VWMD. Does brain-specific MCL-1 deficiency starting at the age of 10 months (using CreERT mice) cause CNS abnormalities in adult mice?*

We agree that Mcl-1 deletion in our model disrupts postnatal brain development. Our studies show that in early life, oligodendrocytes depend on MCL-1 to prevent spontaneous apoptosis. It is an interesting, but separate question whether Mcl-1 deletion induced in the adult would also cause a similar phenotype. The suggested studies would take over a year to conduct, and while they are of interest, they are not required to prove our main point, which is that developmental leukodystrophies may result from the dependence of oligodendrocytes on MCL-1. In the revision, we will state that our comparison on the Mcl-1-deletion phenotype to VWMD is hypothetical, and that additional studies are needed to test this hypothesis.

• Does MCL-1 deletion exacerbate the pathology in eIF2B5 R132H/R132H mice? Moreover, does MCL-1 overexpression rescue the pathology in eIF2B5 R132H/R132H mice? These two experiments are necessary to demonstrate the involvement of MCL-1 in VWMDpathogenesis.*

We agree that these are interesting and important studies; however, these studies will require years to complete and extensive resources. These studies are not needed to show that Mcl-1 deletion produces early onset white matter degeneration, which is our main point. As in our response to point 7 above, we will state in the revision that our comparison on the Mcl-1-deletion phenotype to VWMD is hypothetical, and list these experiments as follow up studies that are needed to test this hypothesis.

*Reviewer #3 (Significance (Required)):

The study will not significantly advance the understanding of VWMD pathogenesis.*

We recognize that our assertion of a direct relevance to VWMD was premature, and that additional studies, beyond the scope to this project, are needed to determine if MCL-1 deficiency contributes to VWMD pathology. We agree that the available data do not yet inform VWMD pathogenesis, but these data may become relevant to VWMD as follow-up studies are conducted. The data remain highly relevant to the broad group of leukodystrophies as they demonstrate a physiologic vulnerability of oligodendrocytes that sets them apart from astrocytes and neurons, and thus may play a role in disorders in which oligodendrocyte pathology is central.

Neuroscientists may be interested in the reported findings.

We appreciate the reviewer noting the significance for neuroscience.

My field of expertise: oligodendrocyte, myelin, neurodegeneration, ER stress

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9. A. Trimouille, F. Marguet, F. Sauvestre, E. Lasseaux, F. Pelluard, M. L. Martin-Negrier, C. Plaisant, C. Rooryck, D. Lacombe, B. Arveiler, O. Boespflug-Tanguy, S. Naudion, A. Laquerriere, Foetal onset of EIF2B related disorder in two siblings: cerebellar hypoplasia with absent Bergmann glia and severe hypomyelination. Acta Neuropathol Commun 8, 48 (2020).
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13. L. Kantor, D. Pinchasi, M. Mintz, Y. Hathout, A. Vanderver, O. Elroy-Stein, A point mutation in translation initiation factor 2B leads to a continuous hyper stress state in oligodendroglial-derived cells. PLoS One 3, e3783 (2008).
14. Y. Cabilly, M. Barbi, M. Geva, L. Marom, D. Chetrit, M. Ehrlich, O. Elroy-Stein, Poor cerebral inflammatory response in eIF2B knock-in mice: implications for the aetiology of vanishing white matter disease. PLoS One 7, e46715 (2012).
15. L. Marom, I. Ulitsky, Y. Cabilly, R. Shamir, O. Elroy-Stein, A point mutation in translation initiation factor eIF2B leads to function--and time-specific changes in brain gene expression. PLoS One 6, e26992 (2011).
16. L. C. Fogarty, R. T. Flemmer, B. A. Geizer, M. Licursi, A. Karunanithy, J. T. Opferman, K. Hirasawa, J. L. Vanderluit, Mcl-1 and Bcl-xL are essential for survival of the developing nervous system. Cell Death Differ 26, 1501-1515 (2019).
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23. M. Bugiani, I. Boor, J. M. Powers, G. C. Scheper, M. S. van der Knaap, Leukoencephalopathy with vanishing white matter: a review. J Neuropathol Exp Neurol 69, 987-996 (2010).

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Referee #3

Evidence, reproducibility and clarity

Cleveland et al. tried to argue that brain-specific depletion of apoptosis regulator MCL-1 reproduces Vanishing White Matter Disease (VWMD) in mice. The authors show that brain-specific MCL-1 deficiency leads to brain atrophy, increased brain cell apoptosis, decreased oligodendrocytes, decreased MBP immunoreactivity, and activation of astrocytes and microglia. It is known that VWMD is a hypomyelinating disorder caused by mutation of eIF2B subunits, which displays severe myelin loss but minimal oligodendrocyte apoptosis or loss in the CNS white matter. In fact, a number of studies show increased oligodendrocyte numbers in the CNS white matter. The characteristic oligodendrocyte pathology is foamy oligodendrocytes (Wong et al., 2000), rather than apoptosis. Since the CNS pathology of brain-specific MCL-1 deficient mice is drive by brain cell apoptosis, the relevance of this mouse model to VWMD is very limited. The title of this manuscript is misleading, and should be changed. Moreover, there are a number of major concerns.

1. Figure 1 clearly shows severe atrophy of neocortex in Mcl-1 cKO mice; however, the white matter appears largely normal in the cerebellum and brain stem. Mcl-1 cKO mice also display ventricular dilation and possible atrophy of corpus callosum. The authors should discuss severe atrophy of neocortex in Mcl-1 cKO mice and the possibility that ventricular dilation and corpus callosum atrophy result from severe atrophy of neocortex?
2. The motor and sensory tests in Figure 2 are potential interesting, but their relevance to myelin abnormalities is limited. The authors should perform the behaviors tests that are highly relevant to myelin abnormalities.
3. It is well expected that there are increased apoptotic cells in the brain of Mcl-1 cKO mice. The authors should perform double labeling to demonstrate which cell types undergo apoptosis: neurons, oligodendrocytes, or other cell types? On the other hand, Figure 3A shows that there are substantial apoptotic cells in the cerebral cortex, which is consistent with severe cerebral cortex atrophy in Mcl-1 cKO mice, suggesting neuron apoptosis in the cerebral cortex. Neuron apoptosis would further rule out the relevance of Mcl-1 cKO mice to VWMD.
4. Figure1, 4 the authors use H&E staining to demonstrate white matter loss. H&E staining is good to show general CNS morphology; however, it is impossible to use H&E staining to quantify the integrity of the white matter. The authors should perform specific staining to quantify white matter loss in the mouse models.
5. Figure 5, MBP IHC is good to show general myelin staining, but is not a reliable assay to quantify myelin integrity in the CNS. The authors should perform electron microscopy analysis to quantify myelin integrity in the CNS in the mouse models.
6. Figure 6, SOX10 is a marker of oligodendrocytes and OPCs. The authors should quantify the number of oligodendrocytes (using oligodendrocyte markers, such as CC1) and the number of OPCs (using OPC markers, such as NG2). Does deletion of BAK or BAX reduce oligodendrocyte apoptosis in the CNS of Mcl-1 cKO mice?
7. The authors show that the level of MCL-1 is comparable in brain lysates of wildtype and eIF2B5 R132H/R132H mice at the age of 7 months, and moderately decreased in eIF2B5 R132H/R132H mice at the age of 10 months. VWMD is a developmental disorder. Similarly, brain-specific MCL-1 deficiency causes developmental abnormalities in the CNS. The normal level of MCL-1 in 7-month-old eIF2B5 R132H/R132H mice strongly suggests that MCL-1 is not a major player involved in the pathogenesis of VWMD. Does brain-specific MCL-1 deficiency starting at the age of 10 months (using CreERT mice) cause CNS abnormalities in adult mice?
8. Does MCL-1 deletion exacerbate the pathology in eIF2B5 R132H/R132H mice? Moreover, does MCL-1 overexpression rescue the pathology in eIF2B5 R132H/R132H mice? These two experiments are necessary to demonstrate the involvement of MCL-1 in VWMD pathogenesis.

Significance

The study will not significantly advance the understanding of VWMD pathogenesis.

Neuroscientists may be interested in the reported findings.

My field of expertise: oligodendrocyte, myelin, neurodegeneration, ER stress

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, the authors characterize the phenotype associated with brain-specific deletion of the mcl-1 gene in mice as a model for vanishing white matter-like disease in humans. Unfortunately, the gfap gene is expressed in many cell types during development which are outside of the intended cell type for this study, so functional data presented from the mutant mice is open to interpretation. The authors have not ruled out other interpretations of their results. The authors need to address major shortcomings in their data interpretation by addressing the following issues.

On line 57, the authors indicate that seizures are common in leukodystrophy. This is controversial. Patients may have attacks that look like seizures, but without EEG recordings there is no way to distinguish these events from myoclonus. The authors should note this ambiguity.

On line 58, the authors indicate the absence of treatments for leukodystrophies. The authors should review the following articles: PMID: 7582569, 15452666 and 27882623, and moderate the text.

The methods section is lacking in details in several areas. For example beginning line 136, there is virtually no indication of the MRI details without going to secondary literature. The authors should provide a brief description including magnet strength, type of imaging and the general sequence, software used to collect and analyze the images. Were the brains actually harvested fresh, where mechanical stresses easily deform brain structure, prior to immersion fixation for 48h? This could be troubling despite the method being previously published.

Beginning on line126, the authors could at least indicate the fixative details and whether the mice were perfused or tissue was immersion fixed. Compare this lack of detail with the description of lysis buffer beginning on line 158.

Behavioral testing at young ages is rather problematic regarding data interpretation. For example, open field testing (Fig. 2B) at postnatal day 7, which relies on visual cues, is rather dubious when mice do not open their eyes until 12-13 days after birth. How would the pups know if they were in the middle of an open field and exhibit thigmotaxis, even if they were capable of the behavior at such a young age? Thus, the P7 data likely cannot be interpreted in terms of the knockouts being normal. By P14, when the mutants exhibit a phenotype, they are already significantly underweight, which can lead to non specific phenotypes such as retinal dysfunction or degeneration. Did the authors look for pathological changes in the retina?

Further, GFAP is expressed in retina of many vertebrate species (PMID 1283834) which would inactivate mcl1 in that tissue and possibly lead to blindness. Indeed, the table at the following link provides a list of tissues in which the gfap-cre transgene is expressed during development. The authors need to address this major issue. http://www.informatics.jax.org/allele/MGI:2179048?recomRibbon=open

For the startle response, which relies on normal hearing, did the authors check to determine if the mutants are deaf? This is very difficult at such a young age, especially prior to tight junction assembly in the lateral wall at around P14. Again, GFAP is expressed in the cochlea at an early age (see PMID 20817025) and may have caused degenerative pathology in this tissue. The authors need to address this major issue.

Significance

Unknown.

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Referee #1

Evidence, reproducibility and clarity

Comments

1. MCL-1 promotes the survival of different cell lineages through its ability to inhibit the pro-apoptotic proteins BAK and BAX, the main effectors of cell death in mammalian cells. By depleting brain cells of MCL-1, apoptosis is promoted in these cells, as confirmed by histopathology of the mouse brain. This is, however, a nonspecific process. Depletion of MCL-1 in any tissue would promote apoptosis in cells of this tissue and general knock-out is known to cause embryonic lethality. So, it is no surprise that knock out of MCL-1 in brain cells leads to a brain disease.
2. The white matter disease is interpreted as similar to VWM; VWM is specifically investigated and MCL-1 is found to be decreased in VWM brain tissue. The decrease is most likely nonspecific. Decrease in MCL-1 is most likely part of a general mechanism of degeneration of brain tissue or white matter. That is a different but also important conclusion. It is essential that other progressive leukodystrophies and acquired brain diseases with tissue degeneration, such as encephalitis, are investigated as well to see whether MCL-1 is also decreased in these disorders. If so, the MCL-1 decrease in white matter disease and other brain degenerative disease should be described as a final common pathway rather than specifically applicable to VWM.
3. Adding to point 2 is the fact that the pathology of the brain-specific MCL-1 knock-out mouse does not resemble the pathology of VWM at all. The central features of VWM are abnormal astrocyte morphology with astrocytes having a few stunted processes, lack of reactive astrogliosis, lack of microgliosis, increase in number of oligodendrocytes and presence of foamy oligodendrocytes. The increase in oligodendrocytes in VWM may be such that the high cellularity leads to diffusion restriction on MRI. Bergmann glia are typically ectopic, but not reduced in number. By contrast, the brain-specific MCL-1 knock-out mouse is characterized by decreased numbers of oligodendrocytes, increased numbers of microglia, reactive astrogliosis, decreased numbers of Bergmann glia and ectopic granule cells. No morphological abnormalities of oligodendrocytes and astrocytes are observed. So, histopathologically the only shared feature is preferential involvement of the brain white matter.
4. The clarity of the work would benefit from a different approach to introduce the study. It would help the reader to know that (1) gray matter cell specific Mcl-1 deletion in mice did not cause apoptosis and (2) apoptosis may have different effector proteins. This important information is now in the discussion. The switch to another cell type in the brain (hGFAP+ cells) would be logical and the significance of the work may improve. When approaching the topic from the field of leukodystrophies one would not necessarily think of deleting the Mcl-1 gene, especially as this gene is not associated with any known leukodystrophy and tends to associate with preneoplastic and neoplastic disease.
5. The authors claim that the ISR is activated in VWM, which means that eIF2α phosphorylation levels are increased, general protein synthesis is decreased and a transcription pathway is regulated by ATF4 and other factors. However, this is not what is seen in VWM. Increased eIF2α phosphorylation and reduced general protein synthesis are not observed in VWM; strikingly, the level of eIF2α phosphorylation is reduced, general protein synthesis appears at a normal rate, and only the ATF4-regulated transcriptome is continuously expressed in VWM astrocytes. Fritsh et al. show that MCL-1 protein synthesis is reduced by increased eIF2α phosphorylation due to reduced translation rates at the Mcl-1 mRNA and not due to differences in Mcl-1 mRNA levels. One would a priori not expect to find altered MCL-1 synthesis rates in the mildly affected VWM mouse model Eif2B5R132H/R132H. Actually, ISR deregulation has not been reported in the Eif2B5R132H/R132H VWM mouse model. The authors need to rephrase this part of their study taking this information into account, when explaining their experiments and interpreting their results. The authors now imply that their study adds mechanistic insight into the VWM field and that is not the case. In addition, Figure 7C shows differences in actin signal rather than MCL-1 signal, suggesting that transfer of the actin protein from the gel to the blot was not optimal for the middle lanes. MCL-1 protein may thus not be reduced in these samples from Eif2B5R132H/R132H VWM mice.
6. Can the authors show in which cell type was apoptosis found (lines 315-316)? Their study uses the hGFAP - Cre mouse model to generate conditional Mcl-1 knock-out mice. The original paper by Zhuo et al. describing the hGFAP - promoter mouse model suggests that Mcl-1 expression is also affected in neurons and ependymal cells. The authors can investigate this further to assess which cell types (1) are sensitive to apoptosis by Mcl-1 deletion and (2) depend on Bax and Bak.
7. Heterozygous deletion of Bak greatly reduces the number of Bak-expressing cells (Fig. 3C, line, 331-333). Authors need to explain this remarkable finding. Please provide raw IHC data. Co-staining with neuronal, astrocytic or oligodendrocytic markers would be insightful. In addition, what does the Western blot signal for the BAX protein represent in Bax homozygous knock out mice (Fig. 3C)? Can the percentage of BAX+ cells in Mcl-1/BaxdKO corpus callosum be determined, similarly as was done for BAK? Co-staining with neuronal, astrocytic or oligodendrocytic markers would be insightful here as well. The legend of Fig. 3D does not state what staining is shown (H&E?).
8. What explains the strong GFAP expression in processes of Mcl-1 KO astrocytes? Are these cells refractory to apoptosis or to hGFAP-driven Cre expression and recombination? Do they lack BAK or BAX or other apopotic-regulating protein? Or do specific factors compensate for the loss of MCL-1?
9. Which developing symptoms do the authors refer to in line 468? Please specify and introduce appropriate references.
10. The definition of leukodystrophies given in the paper is outdated. Leukodystrophies are not invariably progressive and fatal disorders. For more recent definition of leukodystrophies see Vanderver et al., Case definition and classification of leukodystrophies and leukoencephalopathies, Mol Genet Metab 2015, and van der Knaap et al., Leukodystrophies a proposed classification system based on pathology, Acta Neuropathol 2017.
11. It is not correct that there is no specific targeted therapy clinically implemented to arrest progression of the disease in any leukodystrophy. Perhaps hematopoietic stem cell transplantation is not specific targeted, although curative if applied in time in adrenoleukodystrophy and metachromatic leukodystrophy, but certainly genetically engineered autologous hematopoietic stem cells would qualify the definition. In any case, the suggestion that no leukodystrophy is treatable is not correct.

Significance

see above

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Reply to the reviewers

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

The authors aimed to understand the control and the elimination of disseminated tumor cells by NK cells within the lung, their main question being how pulmonary NK cells are able to prevent tumor cells from colonization in the lung.

To dissect this question, Hiroshi Ichise and colleagues took advantage of the ultra-sensitive bioluminescence whole body imaging system combined with intravital two-photon microscopy technology involving genetically-encoded biosensors tumor or NK cells to explore the behavior and functional competences of NK cells in an experimental lung metastasis model.

First, the authors have monitored the fate of intravenously injected B16-Akaluc cells from 5 min to 10 days and observe that tumor cells decrease rapidly within the first 12-24 hours. In parallel, they performed asialoGM1+ and NK1.1+ cells depletion by injection of depleting anti-aGM1 and anti-NK1.1 antibodies in order to see the involvement of these populations on the elimination of the disseminated tumor cells. They conclude that a rapid decrease of the tumor cells is mediated by NK cells. Consisting with this first data, the authors observe also the same early NK cells mediated impact on two other syngenic mouse tumor cell lines : the BRAFV600E melanoma and the colon adenocarcinoma MC-38.

In a second part, the authors dissected NK cell dynamic behaviors in the pulmonary capillaries by taking advantage of the NKp46iCRExrosa26dtTomato mice where NKp46+ cells are fluorescents and performed 2P intravital imaging to follow the in situ the NKp46+ cells behavior. They could nicely observe that NK cells arrive from the capillaries and patrol on the lung epithelial cells in a stall-crawl-jump manner. Moreover, they also show that the attachment to the pulmonary capillaries is mediated by LFA-1. In the presence of B16F10 tumor model, they observe that NK cells stay longer in the capillaries and increase their duration time of crawling indicating that NK cells stay in contact longer with tumor cells.

The authors then explored the NK-mediated tumor killing in the lung by measuring tumor cell apoptosis using B16F10-SCAT3 cells (which leads to visualize caspase 3 activation) and Ca2+ influx in tumor cells expressing two Ca2+ sensors, GCaMP6s and R-GECO. They could observe casp3 activation but also Ca+ influx on tumor cells within few minutes after encountering NK cells. They also observe that evasion of NK cell surveillance is mediated by Nectin-5 and Nectin-2 expressed on tumor cells.

Then, they focus on NK cell activation by looking at ERK activation. To do so, they have isolated NK cells from Tg mice expressing a FRET-based ERK biosensor and performed in vitro killing assay against B16-R-GECO tumor cells but also in vivo experiments. For the in vivo experiments, they have developed reporter mice whose NK cells express the FRET biosensor for ERK. They observe that ERK-dependent NK cell activation contributes to the elimination of disseminated tumor cells within the first few hours but not after 24hours. Indeed, theu observe that B16F10-Akaluc tumor cells are equally eliminated when injected 24h after a first injection of B16F10 or PBS in mice. The authors concluded that tumor cell acquire the capacity to evade NK cell surveillance after 24h rather than a hypothesis toward NK cells loose tumoricidal activity over time.

Finally, the authors have explored their last result on the potential tumor cell evasion of the NK cell surveillance. They show that this NK cell evasion is mediated by the shedding of cell surface Necl-5. They next show that clivage of extracellular domain of Necl-5 was mediated by thrombin in vitro and that anti-coagulation factors such as Warfarin, Edoxaban or Dabigatran Etexilate promote tumor elimination as observed by the bioluminescence experiments. This loss prevents the NK cell signaling needed for effective killing of tumor targets.

However, most of the results remain correlations and have not been formally demonstrated or miss controls.

B16F10 is a well known and characterized NK cell target in a in vivo model so the first part is not really knew except the in situ behavior of NK cells within the lung capillaries. The new mecanism of thrombin-mediated shedding of Necl-5 causing evasion from NK Cell surveillance is really concentrated on the last figure (Fig N{degree sign}6) and some supplemental experiments are mandatory and needed to really confirm this affirmation.

Response: We deeply appreciate the reviewer’s effort to evaluate our work. The reviewer criticizes that the mechanism is well known except “the in situ behavior of NK cells within the lung capillaries.” Indeed, this is what we wish to emphasize in our work. Nobody has ever seen how NK cells kill metastatic tumor cells in the lung. There is a big GAP between in vitro tissue culture experiments and in vivo macroscopic counting of metastatic nodules. Most researchers do not even know when and where in the lung NK cells kill metastatic tumor cells. Live imaging is a powerful approach to address such questions.

Reviewer #1 (Significance (Required)):

There are several points to address to improve the significance of these data.

\*Major points***

1) A global point : 3 mice/group is to small to analyse and interprete data because of the heterogeneity of the mice. Mean +/- SEM have to represented instead of SD.

Response: For the sake of animal welfare, researchers are asked to use minimal number of mice. Moreover, only one mouse can be observed in each imaging session, which takes several hours. In most experiments we performed two independent experiments with three mice each. We believe, the number is appropriate for this type of experiment. In the case of small number of samples, we think SD is better than SEM.

2) The authors used the well known polyclonal anti-asialoGM1 Ab to deplete NK cells. AsialoGM1 is also expressed by ILC1, T, NKT and gd+T cells but also basophils (Trambley J et al., Asialo GM1(+) CD8(+) T cells play a critical role in costimulation blockade-resistant allograft rejection. JCI, 1999). The authors checked the involvement only for the basophils. They have to check the depletion of each of these populations specifically in the lung to assume that the depletion impact only the NK cells or they must change their conclusion on the entire manuscrit and say that not only NK cells is responsible and involved in the control of the disseminated tumor cells but maybe also ILC1, NKT and or gd+T cells.

Response: We obtained similar observations by using BALB/c nu/nu mice, which lack T cells. Therefore, we can exclude the contribution of T cells at least in the acute phase (*3) Lines 133 to 136 : The authors say that they « did not observe any significant difference in the relative increase of the bioluminescence signal between the control and αAGM1-treated mice, implying that NK cells eliminate disseminated melanoma cells primarily in the acute phase (Response: After 24 hrs, the slope of increment of bioluminescence intensity (BLI) did not change significantly betweenαAGM1-treated mice and control mice. In both mice, the doubling times of melanoma cells are approximately one day.

4) Fig S3A-B : The authors say that basophils express aGM1 so they performed basophils involvement on the elimination of B16F10 tumor cells with depleting aCD200R3 mab. They also checked the involvement of neutrophils and monocytes. They observed that basophils, neutrophils and monocytes are not involved on the B16F10 elimination. But what is the hypohesis to assess the role of neutrophils and monocytes ? Moreover, they did not explore Basophil roles in the other models including MC-38, BRAFV600E and 4T1 tumor cells.

Response: We depleted neutrophils and monocytes because antibody-mediated removal of leukocytes could have non-specifically increased the survival of tumor cells. As for expanding the number of experiments with different cell lines, we are afraid but it is too much burden, considering the period required for the experiments and animal welfare.

5a) Fig 1D : Missing control : the author must add the WT Balbc + a-AGM1 as control.

Response: We have this data, which will be included in the revised paper.

5b) Lines 154 to 156 : the authors say that « T cell immunity does not contribute to tumor cell reduction » because tumor cells are eliminated in the nu/nu mice as efficiently as in the WT Balbc mice. This is not correct because they are looking in a window that correspond to innate immunity activation (up to 24h) so they cannot talk about T cell immunity, the adpative response will come more later around 8 days after.

Response: Yes, we are focusing on the early phase of the rejection of metastatic tumor cells. We will rephrase the sentences.

6) Line 159 : (refer to point #2) To affirm that NK cells is critical and involved in the elimination of the disseminated tumor, authors have to perform experiment in a model of NK cell deficiency. The most relevant nowaday is the NKp46ICRExrosa26DTA mice that are deficients in NK cells but also ILC1 cells. Indeed, the authors have used the NKp46iCre mice model for other questions.

Response: As the reviewer stated, the contribution of NK cells in the rejection of metastatic tumors is very well known. We do not think we need to repeat the experiments by using other genetically modified mouse lines, which will take at least one year. We wish to emphasize again that the new findings of our paper are in the in vivo imaging.

7a) Fig 2F : IC missing

Response: According to the reviewer's suggestion, we will perform control experiments with an isotype control.

7b) Lines 181-182 : Authors conclude that the effect of anti-LFA-1 on NK cells adhesion to the pulmonary endothelial cells is mediated primarily by LFA-1. It is not totally true because it is partially mediated as observed in the fig 2F. So authors should change their conclusion and precise that the involvement is partially mediated by LFA-1.

Response: We will rephrase the result section in the revised paper.

8) Fig S5B-C-D and S7: The authors talk about tumor cell death. But they are analyzing Ca2+ influx in vitro so it is a little bit different from the cell death. I'm wondering how the cell death is mesured espacially in the fig S5D and S7?

Response: Under microscopes, apoptosis can be easily recognized by the appearance of blebs. We will include videos in the revised paper.

9) Fig 4H and lines 232-233 : the authors conclude that « damage to tumor cells is dependent on the engagement of DNAM-1 on NK cells ». There is any experiment performed to affirm this point so the authors cannot maintain this conclusion. First, the authors only analyzed Ca2+ influx at a specific time point. So this result only show that Nectin-5 and/or Nectin-2 expressed by B16F10 is involved in the Ca2+ influx following NK cell contact but there is any data on DNAM-1 contribution. So, the role on the NK cells and specifically DNAM-1+ NK cells have not been adressed here. To answer to that question, the author have to perform in vivo model of engrafted WT vs Necl-5/2 ko B16F10 in a WT vs DNAM1 deficient NK cells mouse model to ascertain the contribution of Necl-5/2-DNAM-1 on NK cells. Moreover, survival curve and bioluminescent experiments would be very appreciated.

Response: We have shown the data with Necl-5/Nectin-2-deficientB16F10 cells in Fig. S7. I understand the importance of the experiment with the DNAM-1-deficient mice. But the introduction of another knockout mouse line cannot be performed easily. Instead, we will tone down the conclusion on the requirement of signaling from Necl-5/Nectin-2 to DNAM-1.

10) Lines 253-254 : the authors talk about tumor apoptosis but they are looking at Ca2+ influx. So, they should change their conclusion or show killing experiment.

Response: In Figure S7, we have shown that the sustained Ca2+ influx is a useful surrogate marker for apoptosis. We will include this information explicitly in the revised paper.

11) Fig 6 : the authors conclude that the trombin dependent shedding of Necl-5 causes evasion of NK cells surveillance. Moreover, all experiments are correlations and do not implicate in the same experiment Necl-5, DNAM-1+ NK cells and trombin or anti-coagulation factors. So, as in the comment #9, to adress this point, the authors should inject WT vs Necl-5 deficient B16F10-Akaluc into WT vs NK cell depleted mice and monitor the bioluminescence of the tumor cells within 24h following injection of anti coagulation factors as in the fig 6H. Moreover, the monitoring of the survival curve and the number of the lung metastasis would be also very important and informative to really answer to this point.

Response: We will try the requested experiments during revision.

\*Minor points***

1) Fig 2E: The authors assess the involvement of LFA-1 and MAC-1 on the NK cells attachement to the the pulmonary endothelial cells. But there is other adhesion molecules that are known to be expressed by NK cells as for example CR4 (CD11c/CD18). So, the attachement of NK cells could be also due to this molecule.

Response: We agree. The text will be modified to suggest the involvement of other adhesion molecules.

2) Lines 190 to 197 : Authors should put this methodology part in the « material and method » in order to be more clear on the message they want to deliver.

Response: We will modify the text according to the suggestion.

3) line 228 : There is any hypothesis or explanation regarding the use of Necl5/Necl2 deficient B16F10. Why authors decided to go and explore this pathway ? Authors could add some transition sentence and explanation to help readers.

Response: We will refer to previous papers suggesting the role of DNAM-1 and its ligands, Necl-5 and nectin-2.

4) The author could performed the same experiment as in Fig S7D and assessed ERK activation of DNAM+ vs - NK cells against WT vs Necl-5/Necl-2KO R-GEKO B16F10 cells.

Response: We will try the suggested experiments.

5) Line 283 : Thanks to reformulate the sentence. Check the firgures associated with the text.

Response: We will correct this error. The figures will be Fig. 5E and 5F.

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

The authors use in vivo imaging techniques to investigate the killing of lung metastasis by NK cells. They demonstrate that the cleavage of CD155 may result in resistance of killing by NK cells and suggest that this could be an immune evasion mechanism of metastatic tumor cells.

Overall, the subject is highly relevant, and the in vivo imaging is an interesting and highly relevant technique. However, the message, that tumor cells escape the killing by NK cells by cleavage of CD155 is interesting, but not yet fully supported by the data.

\*Major comments:***

1. • Figure 6: To support their main claim the authors would need to transfect the tumor cells with a CD155 mutant, which cannot be cleaved by Thrombin and show that these tumor cells can no longer escape NK cell-mediated killing. This experiment is straight forward and feasible. Another important experiment along this line would be the use the CD155/CD112 deficient tumor cells (Which the authors use in figure 4) in the experiments shown in figure 1. One would expect that tumor control by NK cells within the first 24h is absent when using these tumor cells.* Response: We previously made five CD155 mutants, which could be resistant to thrombin-mediated cleavage, and re-expressed in CD155/CD112 deficient tumor cells. However, none of the mutants was not killed by NK cells both in vivo and in vitro. It appears that the potential thrombin-cleavage site(s) reside in the recognition site by DNAM-1. We will include this observation in the discussion.

• Figure 5: The demonstration that ERK is activated in this in vivo setting is novel. However, ERK activation is not DNAM-1 specific and the ERK inhibitor is significantly less effective that the depletion of NK cells. Therefore, the relevance of these data to the main message of the manuscript is unclear and the figure could be omitted.*

Response: We agree that the modest effect of MEKi implies that ERK activation is dispensable for NK activation. However, ERK activation is a useful marker of NK cell activation. The data shown here vividly show the timing of NK cell activation and following tumor cell killing. Because the in vivo dynamics of NK cell activation and tumor cell killing is the most important message of this work, we wish to show this data.

• In general, the issue of NK cell exhaustion should be addressed in more detail. The experiments do not address serial killing activity of NK cells and more data is needed to show that it is not an exhaustion of NK cells but the cleavage of CD155 from the tumor cells that prevents further killing.*

Response: We believe, Fig. 5G clearly shows that NK cells are not exhausted 24 hours after tumor cell injection.

**Minor comments:**

• Figure 1C: The relevance of this experiment needs to be better explained.*

Response: We will rephrase the result section in the revised paper.

• Figure 3A: What does SHG stand for?*

Response: It is shown in line 625, M&M section. We will show the statement that SHG stands for second harmonic generation channel in the figure legend.

• Figure 3: Please add a statistical analysis for these experiments.*

Response: We will include P values in the revised paper.

• Figure 4: The use of the caspase-3 and the calcium sensors may detect different cytotoxic mechanisms used by the NK cells. While caspase-3 can be activated by death receptor and perforin/granzyme B mediated killing, the calcium sensor may report mostly on perforin mediated membrane damage. These killing mechanisms have different kinetics and are differentially used during serial killing by NK cells. This should be addressed (at least in the discussion).*

Response: We thank this invaluable comment. We will include this discussion.

Reviewer #2 (Significance (Required)):

Investigating the in vivo cytotoxicity of NK cells against tumor cells by using live imaging technologies is highly relevant for the understanding of the dynamic relationship between tumor and killer cells. Therefore, the subject of this manuscript and the technologies used are very relevant, as in vivo killing activities do not always translate to the in vivo setting.

Response: We thank the reviewer for the favorable comment.

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

\*Summary***

Ichise et al., present a solid work describing the modality and time frame of action of NK control over seeding metastatic cells within the lung vasculature. Th authors use a variety of technique able to dissect how NK patrol lung vasculature, that they interact with cancer cells as they interact with the endothelial cells and they activate a ERK dependent activation leading to calcium influx in cancer cells leading to their death. The data support the notion that this NK control occur over an early time frame, 4h after cancer cells arrival and is mediated by Necl expression on cancer cells. After this time point cancer cells show a thrombin dependent loss of Necl expression on their surface and therefore become resistant to NK control.

\*Comments:***

The data presented are supporting the conclusions. This work utilizes a variety of elegant strategy combining reporter strategy with in vivo imaging to assess the phenomenon of interaction, ERK activation, Calcium Inflax and Apoptosis activation directly in the lung.

In term of experiments, I found the work thorough and complete.

The data a presented well overall and the statistics seems adequate.

I only have few suggestions:

Supplementary Figure S3, show the use of antiLy6G to deplete neutrophils in the lungs of C57BL/6 mice injected with melanoma B16F10 cells. It was recently shown that this antibody is not efficient in depleting neutrophils in this background, but only lead neutrophils to internalise the Ly6G so they cannot be detected by FACS. As shown in Boivin et al 2020 http://doi.org/10.1038/s41467-020-16596-9) neutrophils depletion in C57BL/6 mice can be achieved by using antiGr1 antibody. Therefore, if the authors aim to show this additional control, which I also agree is really good to have, I suggest performing the experiment accordingly to the best-known practice.

Response: We will perform the suggested experiment.

Figure 1E: in the text the experiment is described as 4T1 Akaluc cells were inoculated into the foot pad of BALB/c mice with either control antibody or αAGM1, but the legend states that mice subcutaneously injected with B16 Akaluc cells into footpad.

As B16 melanoma cells are not in BALB/c background, I assume the legend needs to be corrected as the cells should be 4T1, however I wonder if injecting 4T1 breast cancer cells in the footpad could have let to the substantial growth required for lung metastasis without impairing the animal mobility. Could it be that cells where actually injected in the fat pad of the mice and this is just a misspelling in the text?

In this case, the different in the tissue residence NK cells could also potentially explain why 4T1 are not cleared in the fat pad like the B6 cells are in the footpad.

The authors should comment on the difference in the in clearance of the cells at the injection site in Figure 1C VS Figure 1E.

Response: We apology the erratum in the legend.

Figure 1C was performed to examine whether NK cells in the lung could be exhausted or inert 14 days after the inoculation of B16F10 cells. In this experiment, Akaluc-expressing B16F10 cells were inoculated to monitor the bioluminescence for 24 hrs.

In figure 1E, we used Akaluc-expressing 4T1 breast cancer cells because 4T1 cells inoculated into footpad can be spontaneously metastasized to the lung (Kamioka et al., 2017). We observed the bioluminescence of 4T1 cells in the lung for up to 20 days.

Ref: Kamioka, Y., Takakura, K., Sumiyama, K., and Matsuda, M. (2017). Intravital FRET imaging reveals osteopontin-mediated polymorphonuclear leukocyte activation by tumor cell emboli. Cancer Sci 108, 226-235.

Reviewer #3 (Significance (Required)):

The present work is highly relevant to the field of cancer metastasis. While it is known that NK are responsible for the first line of defence against metastatic seeding, most of the studies focuses on how they are suppressed or influenced by other immune cells. The present study provides a very accurate description of their mechanism of action, how they depend in the interaction with the endothelial cells and highlight the novel aspect of thrombin in inducing cancer cells NK resistance. What cause thrombin activation is the next relevant question, by in my opinion this study is complete and important.

My field of expertise is cancer metastasis and their interaction with the immune system and I personally enjoy very much reading this work.

Response: We thank the reviewer for favorable comments and appreciate the effort to evaluate our work.

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Referee #3

Evidence, reproducibility and clarity

Summary

Ichise et al., present a solid work describing the modality and time frame of action of NK control over seeding metastatic cells within the lung vasculature. Th authors use a variety of technique able to dissect how NK patrol lung vasculature, that they interact with cancer cells as they interact with the endothelial cells and they activate a ERK dependent activation leading to calcium influx in cancer cells leading to their death. The data support the notion that this NK control occur over an early time frame, 4h after cancer cells arrival and is mediated by Necl expression on cancer cells. After this time point cancer cells show a thrombin dependent loss of Necl expression on their surface and therefore become resistant to NK control.

Comments:

The data presented are supporting the conclusions. This work utilizes a variety of elegant strategy combining reporter strategy with in vivo imaging to assess the phenomenon of interaction, ERK activation, Calcium Inflax and Apoptosis activation directly in the lung. In term of experiments, I found the work thorough and complete. The data a presented well overall and the statistics seems adequate. I only have few suggestions:

Supplementary Figure S3, show the use of antiLy6G to deplete neutrophils in the lungs of C57BL/6 mice injected with melanoma B16F10 cells. It was recently shown that this antibody is not efficient in depleting neutrophils in this background, but only lead neutrophils to internalise the Ly6G so they cannot be detected by FACS. As shown in Boivin et al 2020 http://doi.org/10.1038/s41467-020-16596-9) neutrophils depletion in C57BL/6 mice can be achieved by using antiGr1 antibody. Therefore, if the authors aim to show this additional control, which I also agree is really good to have, I suggest performing the experiment accordingly to the best-known practice.

Figure 1E: in the text the experiment is described as 4T1 Akaluc cells were inoculated into the foot pad of BALB/c mice with either control antibody or αAGM1, but the legend states that mice subcutaneously injected with B16 Akaluc cells into footpad. As B16 melanoma cells are not in BALB/c background, I assume the legend needs to be corrected as the cells should be 4T1, however I wonder if injecting 4T1 breast cancer cells in the footpad could have let to the substantial growth required for lung metastasis without impairing the animal mobility. Could it be that cells where actually injected in the fat pad of the mice and this is just a misspelling in the text? In this case, the different in the tissue residence NK cells could also potentially explain why 4T1 are not cleared in the fat pad like the B6 cells are in the footpad.

The authors should comment on the difference in the in clearance of the cells at the injection site in Figure 1C VS Figure 1E.

Significance

The present work is highly relevant to the field of cancer metastasis. While it is known that NK are responsible for the first line of defence against metastatic seeding, most of the studies focuses on how they are suppressed or influenced by other immune cells. The present study provides a very accurate description of their mechanism of action, how they depend in the interaction with the endothelial cells and highlight the novel aspect of thrombin in inducing cancer cells NK resistance. What cause thrombin activation is the next relevant question, by in my opinion this study is complete and important.

My field of expertise is cancer metastasis and their interaction with the immune system and I personally enjoy very much reading this work.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

The authors use in vivo imaging techniques to investigate the killing of lung metastasis by NK cells. They demonstrate that the cleavage of CD155 may result in resistance of killing by NK cells and suggest that this could be an immune evasion mechanism of metastatic tumor cells. Overall, the subject is highly relevant, and the in vivo imaging is an interesting and highly relevant technique. However, the message, that tumor cells escape the killing by NK cells by cleavage of CD155 is interesting, but not yet fully supported by the data.

Major comments:

1. Figure 6: To support their main claim the authors would need to transfect the tumor cells with a CD155 mutant, which cannot be cleaved by Thrombin and show that these tumor cells can no longer escape NK cell-mediated killing. This experiment is straight forward and feasible. Another important experiment along this line would be the use the CD155/CD112 deficient tumor cells (Which the authors use in figure 4) in the experiments shown in figure 1. One would expect that tumor control by NK cells within the first 24h is absent when using these tumor cells.
2. Figure 5: The demonstration that ERK is activated in this in vivo setting is novel. However, ERK activation is not DNAM-1 specific and the ERK inhibitor is significantly less effective that the depletion of NK cells. Therefore, the relevance of these data to the main message of the manuscript is unclear and the figure could be omitted.
3. In general, the issue of NK cell exhaustion should be addressed in more detail. The experiments do not address serial killing activity of NK cells and more data is needed to show that it is not an exhaustion of NK cells but the cleavage of CD155 from the tumor cells that prevents further killing.

Minor comments:

1. Figure 1C: The relevance of this experiment needs to be better explained.
2. Figure 3A: What does SHG stand for?
3. Figure 3: Please add a statistical analysis for these experiments.
4. Figure 4: The use of the caspase-3 and the calcium sensors may detect different cytotoxic mechanisms used by the NK cells. While caspase-3 can be activated by death receptor and perforin/granzyme B mediated killing, the calcium sensor may report mostly on perforin mediated membrane damage. These killing mechanisms have different kinetics and are differentially used during serial killing by NK cells. This should be addressed (at least in the discussion).

Significance

Investigating the in vivo cytotoxicity of NK cells against tumor cells by using live imaging technologies is highly relevant for the understanding of the dynamic relationship between tumor and killer cells. Therefore, the subject of this manuscript and the technologies used are very relevant, as in vivo killing activities do not always translate to the in vivo setting.

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 authors aimed to understand the control and the elimination of disseminated tumor cells by NK cells within the lung, their main question being how pulmonary NK cells are able to prevent tumor cells from colonization in the lung.

To dissect this question, Hiroshi Ichise and colleagues took advantage of the ultra-sensitive bioluminescence whole body imaging system combined with intravital two-photon microscopy technology involving genetically-encoded biosensors tumor or NK cells to explore the behavior and functional competences of NK cells in an experimental lung metastasis model. First, the authors have monitored the fate of intravenously injected B16-Akaluc cells from 5 min to 10 days and observe that tumor cells decrease rapidly within the first 12-24 hours. In parallel, they performed asialoGM1+ and NK1.1+ cells depletion by injection of depleting anti-aGM1 and anti-NK1.1 antibodies in order to see the involvement of these populations on the elimination of the disseminated tumor cells. They conclude that a rapid decrease of the tumor cells is mediated by NK cells. Consisting with this first data, the authors observe also the same early NK cells mediated impact on two other syngenic mouse tumor cell lines : the BRAFV600E melanoma and the colon adenocarcinoma MC-38.

In a second part, the authors dissected NK cell dynamic behaviors in the pulmonary capillaries by taking advantage of the NKp46iCRExrosa26dtTomato mice where NKp46+ cells are fluorescents and performed 2P intravital imaging to follow the in situ the NKp46+ cells behavior. They could nicely observe that NK cells arrive from the capillaries and patrol on the lung epithelial cells in a stall-crawl-jump manner. Moreover, they also show that the attachment to the pulmonary capillaries is mediated by LFA-1. In the presence of B16F10 tumor model, they observe that NK cells stay longer in the capillaries and increase their duration time of crawling indicating that NK cells stay in contact longer with tumor cells.

The authors then explored the NK-mediated tumor killing in the lung by measuring tumor cell apoptosis using B16F10-SCAT3 cells (which leads to visualize caspase 3 activation) and Ca2+ influx in tumor cells expressing two Ca2+ sensors, GCaMP6s and R-GECO. They could observe casp3 activation but also Ca+ influx on tumor cells within few minutes after encountering NK cells. They also observe that evasion of NK cell surveillance is mediated by Nectin-5 and Nectin-2 expressed on tumor cells.

Then, they focus on NK cell activation by looking at ERK activation. To do so, they have isolated NK cells from Tg mice expressing a FRET-based ERK biosensor and performed in vitro killing assay against B16-R-GECO tumor cells but also in vivo experiments. For the in vivo experiments, they have developed reporter mice whose NK cells express the FRET biosensor for ERK. They observe that ERK-dependent NK cell activation contributes to the elimination of disseminated tumor cells within the first few hours but not after 24hours. Indeed, theu observe that B16F10-Akaluc tumor cells are equally eliminated when injected 24h after a first injection of B16F10 or PBS in mice. The authors concluded that tumor cell acquire the capacity to evade NK cell surveillance after 24h rather than a hypothesis toward NK cells loose tumoricidal activity over time. Finally, the authors have explored their last result on the potential tumor cell evasion of the NK cell surveillance. They show that this NK cell evasion is mediated by the shedding of cell surface Necl-5. They next show that clivage of extracellular domain of Necl-5 was mediated by thrombin in vitro and that anti-coagulation factors such as Warfarin, Edoxaban or Dabigatran Etexilate promote tumor elimination as observed by the bioluminescence experiments. This loss prevents the NK cell signaling needed for effective killing of tumor targets. However, most of the results remain correlations and have not been formally demonstrated or miss controls. B16F10 is a well known and characterized NK cell target in a in vivo model so the first part is not really knew except the in situ behavior of NK cells within the lung capillaries. The new mecanism of thrombin-mediated shedding of Necl-5 causing evasion from NK Cell surveillance is really concentrated on the last figure (Fig N{degree sign}6) and some supplemental experiments are mandatory and needed to really confirm this affirmation.

Significance

There are several points to address to improve the significance of these data.

Major points

1) A global point : 3 mice/group is to small to analyse and interprete data because of the heterogeneity of the mice. Mean +/- SEM have to represented instead of SD.

2) The authors used the well known polyclonal anti-asialoGM1 Ab to deplete NK cells. AsialoGM1 is also expressed by ILC1, T, NKT and gd+T cells but also basophils (Trambley J et al., Asialo GM1(+) CD8(+) T cells play a critical role in costimulation blockade-resistant allograft rejection. JCI, 1999). The authors checked the involvement only for the basophils. They have to check the depletion of each of these populations specifically in the lung to assume that the depletion impact only the NK cells or they must change their conclusion on the entire manuscrit and say that not only NK cells is responsible and involved in the control of the disseminated tumor cells but maybe also ILC1, NKT and or gd+T cells.

3) Lines 133 to 136 : The authors say that they « did not observe any significant difference in the relative increase of the bioluminescence signal between the control and αAGM1-treated mice, implying that NK cells eliminate disseminated melanoma cells primarily in the acute phase (< 24hrs) of lung metastasis » Please comment because the depletion of asGM1+ cells impact also the growth of the tumor until 8 days (fig 1B-E-G)

4) Fig S3A-B : The authors say that basophils express aGM1 so they performed basophils involvement on the elimination of B16F10 tumor cells with depleting aCD200R3 mab. They also checked the involvement of neutrophils and monocytes. They observed that basophils, neutrophils and monocytes are not involved on the B16F10 elimination. But what is the hypohesis to assess the role of neutrophils and monocytes ? Moreover, they did not explore Basophil roles in the other models including MC-38, BRAFV600E and 4T1 tumor cells.

5a) Fig 1D : Missing control : the author must add the WT Balbc + a-AGM1 as control.

5b) Lines 154 to 156 : the authors say that « T cell immunity does not contribute to tumor cell reduction » because tumor cells are eliminated in the nu/nu mice as efficiently as in the WT Balbc mice. This is not correct because they are looking in a window that correspond to innate immunity activation (up to 24h) so they cannot talk about T cell immunity, the adpative response will come more later around 8 days after.

6) Line 159 : (refer to point #2) To affirm that NK cells is critical and involved in the elimination of the disseminated tumor, authors have to perform experiment in a model of NK cell deficiency. The most relevant nowaday is the NKp46ICRExrosa26DTA mice that are deficients in NK cells but also ILC1 cells. Indeed, the authors have used the NKp46iCre mice model for other questions.

7a) Fig 2F : IC missing

7b) Lines 181-182 : Authors conclude that the effect of anti-LFA-1 on NK cells adhesion to the pulmonary endothelial cells is mediated primarily by LFA-1. It is not totally true because it is partially mediated as observed in the fig 2F. So authors should change their conclusion and precise that the involvement is partially mediated by LFA-1.

8) Fig S5B-C-D and S7: The authors talk about tumor cell death. But they are analyzing Ca2+ influx in vitro so it is a little bit different from the cell death. I'm wondering how the cell death is mesured espacially in the fig S5D and S7?

9) Fig 4H and lines 232-233 : the authors conclude that « damage to tumor cells is dependent on the engagement of DNAM-1 on NK cells ». There is any experiment performed to affirm this point so the authors cannot maintain this conclusion. First, the authors only analyzed Ca2+ influx at a specific time point. So this result only show that Nectin-5 and/or Nectin-2 expressed by B16F10 is involved in the Ca2+ influx following NK cell contact but there is any data on DNAM-1 contribution. So, the role on the NK cells and specifically DNAM-1+ NK cells have not been adressed here. To answer to that question, the author have to perform in vivo model of engrafted WT vs Necl-5/2 ko B16F10 in a WT vs DNAM1 deficient NK cells mouse model to ascertain the contribution of Necl-5/2-DNAM-1 on NK cells. Moreover, survival curve and bioluminescent experiments would be very appreciated.

10) Lines 253-254 : the authors talk about tumor apoptosis but they are looking at Ca2+ influx. So, they should change their conclusion or show killing experiment.

11) Fig 6 : the authors conclude that the trombin dependent shedding of Necl-5 causes evasion of NK cells surveillance. Moreover, all experiments are correlations and do not implicate in the same experiment Necl-5, DNAM-1+ NK cells and trombin or anti-coagulation factors. So, as in the comment #9, to adress this point, the authors should inject WT vs Necl-5 deficient B16F10-Akaluc into WT vs NK cell depleted mice and monitor the bioluminescence of the tumor cells within 24h following injection of anti coagulation factors as in the fig 6H. Moreover, the monitoring of the survival curve and the number of the lung metastasis would be also very important and informative to really answer to this point.

Minor points

1) Fig 2E: The authors assess the involvement of LFA-1 and MAC-1 on the NK cells attachement to the the pulmonary endothelial cells. But there is other adhesion molecules that are known to be expressed by NK cells as for example CR4 (CD11c/CD18). So, the attachement of NK cells could be also due to this molecule.

2) Lines 190 to 197 : Authors should put this methodology part in the « material and method » in order to be more clear on the message they want to deliver.

3) line 228 : There is any hypothesis or explanation regarding the use of Necl5/Necl2 deficient B16F10. Why authors decided to go and explore this pathway ? Authors could add some transition sentence and explanation to help readers.

4) The author could performed the same experiment as in Fig S7D and assessed ERK activation of DNAM+ vs - NK cells against WT vs Necl-5/Necl-2KO R-GEKO B16F10 cells.

5) Line 283 : Thanks to reformulate the sentence. Check the firgures associated with the text.

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Reply to the reviewers

We thank the reviewers for their insightful comments and suggestions. Addressing them will improve our work. Please find below our point-by-points answers to the issues raised. We also provide a partially revised version of the manuscript with changes indicated in blue.

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Reviewer #1 (Evidence, reproducibility and clarity (Required

**Summary**

The authors propose a mechanism through which voltage dependent water pore formation is key to the internalization of Cell permeable peptides (CPPs). The claim is based on an in-silico study and on several experimental approaches. The authors compare 5 peptides (R9, TAT-48-57, Penetratin, MAP and Transportan and use 3 distinct cell lines (Raji, SKW6.4 and HeLa cells), plus neurons in primary cultures. The also present in vivo experiment (mouse skin and zebrafish embryo). All in all, it is an interesting study, but it raises several issues that need to be addressed. Moreover, the length and structure of the manuscript make it very difficult to read (see below under "Reviewer statement")

**Reviewer statement**

The instructions are to use the "Major comments" section to answer 6 precise questions. Unfortunately, this is not possible due to the structure of the document to review. The main manuscript (22 pages) comes with 4 primary figures and 19 supplemental ones. Most of these figures have an enormous number of panels and their legends occupy 17 pages. To this, are added 6 supplemental tables and 7 supplemental movies (with 2 pages of legends), 28 pages of Material and Methods, and 146 References (109 for the main manuscript and 37 for Supplemental information). To be frank, I was often tempted to send the manuscript back, asking for the authors to submit a document facilitating the task of the reviewers.

Because of this complexity, my "Major comments" will come after a page by page, paragraph ({section sign}s) by paragraph and figure by figure "Detailed analysis" of the manuscript.

**Detailed analysis**

Q1. Page 4 {section sign} 3

The test is based on the ability of TAT-RasGAP to kill the cells. Although controls exist, this is worrying since necrotic death might participate in the rupture of the membrane and artificially amplify internalization after a first physiological entry of the peptide. It is also a bit dangerous to add a FITC group to a short peptide without controlling that it has no effect on the interaction with the membrane (FITC-induced local hydrophobicity can provoke peptide tilting and membrane shearing). In the same vein, the very high peptide concentrations often used in the study (40µM for Raji and SKW6.4 cells and 80µM on HeLa cells) can be highly toxic.

A1. We took advantage of the fact that TAT-RasGAP317-326 can kill cells to design a CRISPR/Cas9 screen based on cell survival for the identification of genes encoding proteins involved in CPP uptake. For this purpose, it was important therefore that the peptide was able to kill wild-type cells. Even if we consider the possibility that “necrotic death might participate in the rupture of the membrane and artificially amplify internalization after a first physiological entry of the peptide”, it remains that the cells that survived the screen did so because they were carrying mutations in genes that encoded potassium channels required for CPP uptake. And since the cells that survived the screen, by definition, were not dying, the issue raised by the reviewer is void in this case. The reviewer mentions that we included controls to validate the observations made with FITC-TAT-RasGAP317-326. Indeed, these controls were performed to address the potential problem raised by the reviewer. These controls, listed below, demonstrate that the genes identified through the CRISPR/Cas9 screen were also involved in the uptake of CPPs devoid of killing properties as well as CPPs that were not labelled with fluorophores.

i) Three different cell lines, lacking specific potassium channels identified through the CRISPR/Cas9 screen, were unable to allow a non-labelled, non-toxic CPP (TAT-PNA) to enter cells (Supplementary Fig. 8a).

ii) The Cre recombinase hooked to TAT, a construct that is not labelled with a fluorochrome and that is not toxic, did not enter Raji cells lacking the KCNQ5 potassium channels, also identified through a CRISPR/Cas9 screen (Supplementary Fig. 8b).

iii) The internalization of a TAT-conjugated FITC-labelled cell-protective therapeutic compound was inhibited, sometimes fully, in three different cell lines, lacking specific potassium channels identified through the CRISPR/Cas9 screen (Supplementary Fig. 8c).

Additionally, we are now reporting that the entry of FITC-labelled TAT, R9, and penetratin, all non-toxic CPPs, is impaired in Raji cells lacking the KCNQ5 potassium channel identified in the CRISPR/Cas9 screen. These new results will be incorporated in the revised version of our manuscript.

As supportive evidence that a potential toxicity effect of TAT-RasGAP317-326 is not a confounding factor in experiments recording the initial uptake of the peptide is that internalization is measured after one hour of incubation with the cells (Figure 1), time at which the peptide only minimally impacts the survival of cells (PNAS December 15, 2020 117 31871-31881).

Finally, please note that depolarizing cells, which is what happens in cells lacking the potassium channels identified through the CRISPR/Cas9 screen, not only blocked the uptake of TAT-RasGAP317-326, but also the uptake of a series of non-toxic CPPs (using short-time incubation protocols; Figure 2).

Page 5 {section sign} 1

Q2. Supp. Fig.1a shows no differences between the 3 cell types, even though they differ in their modes of peptide internalization, some favoring vesicular staining and others cytoplasmic diffusion.

A2. The images shown in panel A of this figure depicts, for each cell line, examples of cells that do not take up the CPP, those that only display vesicular staining, and those that additionally take up the peptides in their cytosol. These images were picked to depict these uptake phenotypes and this is why they are similar in the three cells lines. Panel A does not provide any quantitative information on the prevalence of these different uptake modes in the three cell lines. This is shown in panel B of Supplementary Fig. 1. There is, therefore, no discrepancies between the two panels.

Q3. Multiplying cell and peptide types contributes to the complexity of the manuscript without increasing its interest. If there is a conceptual breakthrough, as might be the case, it is obscured by the accumulation of useless images and data. A step into simplifying the manuscript would be (i), to concentrate on Raji cells (leaving out SKW6.4 and HeLa cells) and (ii) to only discuss the R9, TAT (including TAT-RasGAP) and Penetratin peptides.

A3. We are sorry that the inclusion of several cell lines and several CPPs was seen as confusing by the reviewer. Our current vision is that our observations are strengthened if we show that the observed effects are seen in several cell lines and with a variety of CPPs. We would like therefore to not exclude supportive evidence presented in our work because if we do remove some of the data shown in the manuscript, we will definitely weaken some of our claims. We nevertheless remain open with this point that can be further discussed with the editors.

Q4. TAT and R9 are poly-R peptides, which is not the case for Penetratin that has only 3 Rs. These 3 Rs are important (cannot be replaced by 3 Ks), but the two Ws absent in R9 and TAT are equally important as they cannot be replaced by Fs. This must be considered by the authors when they tend to generalize their model.

A4. The point raised by the reviewer concerning the importance of W and R residues in CPPs is well taken. We have now developed this in the discussion with the addition of the paragraphs shown below.

“An additional potential explanation to the internalization differences observed between arginine- and lysine-rich peptides is that even though both arginine and lysine are basic amino acids, they differ in their ability to form hydrogen bonds, the guanidinium group of arginine being able to form two hydrogen bonds1** while the lysyl group of lysine can only form one. Compared to lysine, arginine would therefore form more stable electrostatic interactions with the plasma membrane.

Cationic residues are not the only determinant in CPP direct translocation. The presence of tryptophan residues also plays important roles in the ability of CPPs to cross cellular membranes. This can be inferred from the observation that Penetratin, despite only bearing 3 arginine residues penetrates cells with similar or even greater propensities compared to R9 or TAT that contain 9 and 8 arginine residues, respectively (Supplementary Fig. 9g). The aromatic characteristics of tryptophan is not sufficient to explain how it favors direct translocation as replacing tryptophan residue with the aromatic amino acid phenylalanine decreases the translocation potency of the RW9 (RRWWRRWRR) CPP2. Rather, differences in the direct translocation promoting activities of tryptophan and phenylalanine residues may come from the higher lipid bilayer insertion capability of tryptophan compared to phenylalanine3-5. There is a certain degree of interchangeability between arginine and tryptophan residues as demonstrated by the fact that replacing up to 4 arginine residues with tryptophan amino acids in the R9 CPP preserves its ability to enter cells6. It appears that loss of positive charges that contribute to water pore formation can be compensated by acquisition of strengthened lipid interactions when arginine residues are replaced with tryptophan residues. This can explain why a limited number of arginine/tryptophan substitutions does not compromise CPP translocation through membranes**.”

Q5. Supp. Fig1c-d is not necessary (very little information in it) and Supp. Fig 1e is misleading as it takes a lot of imagination to see a difference between homogenous (top) and focal (bottom) diffusion.

A5. Since we perform cytosolic quantitation to infer direct translocation, it appears important to us, for allowing others to potentially replicate our results, that we precisely report how methodologically we perform our experiments. For Supplementary Fig. 1e, we agree that the examples shown are not easily interpretable. We have now removed this panel, as well as the accompanying panel f, from the Supplementary Fig. 1.

Q6. Supp. Fig.1g: How many cells are we looking at? Given the high variance, the result cannot be interpreted easily. A distribution according to fluorescence bits would be a better way to present the data.

A6. Over 230 cells have been quantitated per condition, which includes all cells where CPP entry has occurred regardless of the intensity or the type of entry. We did not only focus on cells with strong cytosolic staining to avoid any bias with regards to detection limitations. High variance can also be explained by the fact that CPP cellular entry is not synchronized. We tested the way of showing the data as suggested by the reviewer but this did not improve the visualization of the results in our opinion. We will therefore keep the initial presentation. Note that regardless of the way the data are presented, the conclusion remains the same, namely that illumination in our hands is not the cause of CPP membrane translocation.

Q7. Supp. Fig2i. This panel confirms that Raji cells differ from the two other cell types by showing clear temperature dependency. The explanation will come later with the energy barrier for low Vm-induced pore formation. This contradicts earlier reports showing that Penetratin translocation is not temperature-dependent, possibly because it was done on neurons naturally hyperpolarized. Or else because mechanisms are, at least in part, different from the one proposed here for R9 and TAT. This requires some clarification and supports the suggestion that, instead of multiplying models and peptides, it would be more efficient to compare TAT, R9 and Penetratin internalization by Raji cells and primary neurons.

A7. Supplementary Fig. 1i (not Supplementary Fig. 2i as indicated by the reviewer) was reporting the overall CPP uptake, both through direct translocation and endocytosis as a function of temperature. As there is limited endocytosis in Raji cells, the data shown for this cell type mostly correspond to direct translocation. For Hela and SKW6.4, endocytosis is not marginal however and we will perform a new set of experiments to define the role of temperature (4, 20, 24, 28, 32°C) in CPP direct translocation (i.e. cytosolic acquisition) in HeLa cells and SKW6.4 (using the CPPs listed by the reviewer). We have partially performed this for HeLa cells already and this shows that direct translocation is indeed inhibited by low temperatures (more than 10-fold at 4°C compared to 37°C). Bear in mind that no endosomal escape occurs in our settings (see Supplementary Fig. 7c). This indicates that the decrease in cytoplasmic fluorescence induced by low temperature is not a consequence of diminished CPP endocytosis.

Q8. Supp. Fig. 2a-f. Last sentence of the legend "Concentrations above 40µM led to too extensive cell death preventing analysis of peptide internalization". This confirms the warning against the use of concentrations varying between 40 µM and 80 µM and partially jeopardizes the validity of some experiments.

A8. The reviewer has truncated this sentence that actually reads “Note: concentrations above 40 mM of TAT-RasGAP317-326 led to too extensive Raji and SKW6.4 cell death, preventing analysis of peptide internalization at these concentrations.” As different cell lines display various sensitivities to potential toxic effects induced by CPPs (Raji and SKW6.4 cells being more sensitive than HeLa cells for example), we have adapted the concentrations of CPPs used to monitor cellular uptake so that cell death was minimal or non-existent in order to prevent the potential confounding effects mentioned by the reviewer. Hence in contrast to what the reviewer is stating, we are taking care of the toxicity effect and perform our experiments in conditions were toxicity is minimal. The logic of the reviewer to state that we “jeopardize[d] the validity of some experiments” is therefore unclear to us as we did take care of not exposing our cells to toxic CPP concentrations.

Page 6 {section sign} 2

Q9. The authors advocate 2 modes of entry, opposing transport across the membrane and endocytosis. In contrast with R9, TAT and Penetratin, Transportan or MAP seem to be purely endocytosed but, if they reach the cytoplasm, they still have to cross a membrane (unless "a miracle happens"). For Penetratin and R9/TAT, the authors consider that water pore and inverted micelle formation are incompatible. This is a bit rapid as inverted micelles might induce water pores through W/lipids interactions requiring less R residues and, possibly, less energy. This provides the opportunity to signal that, in spite of their very high number, key references are missing or hidden in cited reviews, some of them written by colleagues who are not among the main contributors to the CPP field.

A9. Transportan in our hands indeed appear to enter cells via endocytosis mostly. As reported by the reviewer, how Transportan reaches the cytosol remains unresolved.

Our data support a model where CPPs enter cells via water pores that are not made by the CPPs themselves but that are created by the megapolarization state of the membrane. Our data therefore do not support toroidal or barrel-stave pore models because these pores would be built as a result of CPP assemblage.

Inverted micelles have been hypothesized to mediate CPP translocation across membranes7 but to our knowledge, there is no in silico or cellular experimental evidence for this in the literature. To us, the data on which the involvement of inverted micelle in CPP translocation is based are also fully consistent with the water pore model. CPP translocation through water pores has been seen by several authors during in silico experiments but, to the best of our knowledge, simulations have not reported the formation of inverted micelles during CPP translocation across membranes.

Finally, we would be grateful to this reviewer if the “key references” that are apparently missing from our manuscript are disclosed so that we could acknowledge them appropriately.

Page 7 {section sign} 1

Q10.Fig. 1b confirms that Raji cells provide a good model for loss and gain of function (lovely rescue experiment) and that the authors should drop the two other cell types that provide no decisive information.

A10. Raji and HeLa cells display a stronger direct CPP uptake impairment phenotype when lacking a given potassium channel (KCNQ5 and KCNN4, respectively). In these cell lines, it appears that one potassium channel predominantly controls the plasma membrane potential. In contrast, in SKW6.4 cells, several potassium channels (e.g. KCNN4 and KCNK5) appear to be equally or redundantly involved in the control of the membrane potential. This probably explains the intermediate impact on the Vm and on CPP direct translocation when knocking out a given potassium channel in this cell line. When pharmacologically inducing cellular depolarization, a clear impairment in CPP translocation is however observed in this cell line. Thus, even though the Vm in SKW6.4 cells, is controlled predominantly by several potassium channels, it remains that an appropriate membrane potential is crucially required for these cells to take up CPP across their membrane. We agree with the reviewer that the stronger phenotypic effect observed in Raji and HeLa cells allows easy interpretation. On the other hand, it seems important to us that we provide data reporting intermediate situations so that readers can appreciate the variability that can be observed in different cell lines. Nevertheless, we would like to propose along the reviewer’s suggestion to move the SKW6.4 data from figure 1 to the supplemental data. Feedback from the editors would also be appreciated in this particular instance.

Page 8 {section sign} 1

Q11. A) Supp. Fig. 6b (no serum conditions) allows for the use of "normal" CPP concentrations and suggests that a fraction of the peptides may bind to serum components. No arrows in Supp. Fig.6b (but in 6c), and the R/pyrene butyrate interaction is not in 6c but in 6a. Still for Supp. Fig. 6c, the death of cells at 20µM (or less) even in the absence of K+ channels, confirms that we are borderline in term of peptide toxicity.

B)There is a confusion between Supp. Fig. 6d and 6e and a legend problem (6e is not described). Cell death is assessed in % of PI-positive cells. Does this securely distinguish between death and holes allowing for PI entry without death?

C) The CPP is incubated in the presence of Pyrene butyrate, making the KO cells less resistant. How does that demonstrate that the potassium channels are not involved in the killing if the peptide is already in? Unless the KO is done after internalization (but the cells should be already dead or dying?). This lacks clarity.

A11. We apologize for the lack of clarity in the legend of Supplementary Fig. 6. This will be corrected in the revised version of the manuscript.

A) Supp. Fig. 6b (no serum conditions) allows for the use of "normal" CPP concentrations and suggests that a fraction of the peptides may bind to serum components.

A) The reviewer is correct that CPPs interact with serum components. This is indeed what is reported in this figure. The presence or absence of serum has therefore an important impact in experiments performed with CPPs and should be reported to allow proper interpretation of our data.

No arrows in Supp. Fig.6b (but in 6c), and the R/pyrene butyrate interaction is not in 6c but in 6a.

Thank you for noting this. This is now corrected.

Still for Supp. Fig. 6c, the death of cells at 20µM (or less) even in the absence of K+ channels, confirms that we are borderline in term of peptide toxicity.

It has to be understood that in Supplementary Fig. 6c, we use the TAT‑RasGAP317‑326 peptide that is inducing cell death when translocating into cells8. This cell death response is not provided by the CPP portion of TAT‑RasGAP317‑326 (i.e. TAT) but by its bioactive cargo (i.e. RasGAP317‑326). The read-out in this particular experiment is therefore cell death and this should not be confused with general CPP toxicity.

B) There is a confusion between Supp. Fig. 6d and 6e and a legend problem (6e is not described).

B) This has now been fixed.

Cell death is assessed in % of PI-positive cells. Does this securely distinguish between death and holes allowing for PI entry without death?

The answer to this question is yes. In this manuscript we used PI in two very different experimental set-ups.

i) the conventional cell death detection assay where cells are incubated with 8 mg/ml PI prior to flow cytometry. In this set-up, dead cells with compromised membrane integrity have their nucleus brightly stained with PI.

ii) the detection of small pores in the plasma membrane (water pore) where cells are incubated with ~30 mg/ml PI and the fluorescence of PI measured in the cytosol by confocal microscopy. In this set-up, PI enters into the cytosol through small plasma membrane pores but PI does not stain the DNA in the nucleus. This protocol has been previously described9 and we have further validated it in the present work (Figure 3 and Supplementary Fig. 12).

PI does not fluoresce well unless it binds to DNA. In solution without cells, PI cannot be detected below 128 mg/ml (Supplementary Fig. 12e). At low PI concentrations (8 mg/ml), living cells (even when treated with compounds such as CPPs that create transitory pores) do not display cytosolic PI fluorescence. At high PI concentrations (32 mg/ml), the cytosol of CPP-treated cells becomes PI fluorescent. PI is positively charged and is attracted by the negative membrane potential of the cells. Its movement across the cell membrane is therefore unidirectional. This enables the PI molecules to accumulate/concentrate within the cytosol to values (> 64 mg/ml) allowing its detection (Supplementary Fig. 12a-c). PI and CPPs do no interact (Supplementary Figure 12d); hence they move independently from one another. If PI enters through the water pores induced by CPPs, the entry kinetics of PI and CPPs should be identical. Indeed, this is what we show now in a new figure (refer to our answer #31).

C) The CPP is incubated in the presence of Pyrene butyrate, making the KO cells less resistant. How does that demonstrate that the potassium channels are not involved in the killing if the peptide is already in? Unless the KO is done after internalization (but the cells should be already dead or dying?). This lacks clarity.

C) For the pyrene butyrate experiments the rationale was the following. The CRISPR/Cas9-identified potassium channels could either be involved in CPP internalization or they could be required for the killing activity of TAT-RasGAP317-326 when the peptide is already in the cytosol. To experimentally introduce TAT-RasGAP317-326 in the cytosol and to bypass any potential entry depending on potassium channels, we used pyrene butyrate that efficiently creates an artificial entry route for CPPs into cells. Our data show that when TAT-RasGAP317-326 is introduced in the cytosol through the use of pyrene butyrate, cells died whether they lack specific potassium channels or not. This led to our interpretation that potassium channels are not modulating the cell death activity of TAT-RasGAP317-326 once in the cytosol but that they are required for the entry of the CPP in the cytosol.

Page 9 {section sign} 1

Q12.The conclusion that the diffuse staining does not come from endosomal escape is based on the certainty that LLOME disrupts both endosomes and lysosomes. First, it should be verified with specific markers (rab5, rab7) that the fluorescent vesicles are endosomes. Second, the literature strongly suggests that LLOME primarily disrupts lysosomes and not endosomes. Finally, even if some endosomes are disrupted, the endosomal population is heterogenous and some CPPs may be in a subpopulation insensitive to LLOME. In addition, the importance of this issue is not well explained. In practice, access to the cytoplasm and nucleus requires crossing the plasma and/or the endosomal membrane and the latter, at least in early endosomes (thus the need of identifying the CPP-enriched vesicles), might not be very different from the plasma membrane.

A12. The conclusion that diffuse staining does not come from endosomal escape is based on experiments where HeLa cells were incubated in the presence of CPP for 30 minutes to allow CPP entry into cells, then the cells were washed to prevent further uptake (Supplementary Fig. 7c). We only monitored the cells that initially took up the CPP by endocytosis and not through direct translocation (for the HeLa cell line, there is always a substantial fraction of such cells; see Supplementary Fig. 1b). We measured the cytosolic CPP fluorescence intensity in these cells by time-lapse confocal microscopy for 4 ½ hours. The procedure to do this is now explained in new Supplementary Fig. 7c. We then assessed the CPP fluorescence intensity within the cytosol. No increase in cytosolic fluorescence was detected in this condition, speaking against the possibility that cytosolic acquisition of CPPs by the cells resulted from vesicular escape (the identity of the vesicles being unimportant in this context). Our set-up has the potential to detect CPPs in the cytosol if these CPPs leak out from vesicles because we could measure increased CPP fluorescence in the cytosol in cells treated with LLOME. It did not matter in this positive control experiment what types of CPP-containing vesicles are disrupted by LLOME. What was important to show in this control condition was that the disruption of at least some CPP-containing vesicles permitted us to detect a cytosolic signal.

Page 9 {section sign} 2

Q13. Is Supp. Fig. 7e really necessary? First, as mentioned several times, if 20 µM is a borderline concentration in term of toxicity, raising the concentration up to 100 µM is problematic. Secondly, what matters is not "binding" in general, but binding to the proper membrane components. As mentioned by the authors themselves (Supp. Fig. 1e and movie), there are privileged sites of entry that may correspond to the recognition of specific molecular entities/structures.

A13. The goal of the experiments presented in Supplementary Figure 7e was to determine whether the CRISPR/Cas9-identified potassium channels modulate CPP/membrane interaction. If those channels were to be required for the initial binding of the CPPs to the plasma membrane, this would have not hampered cells to take up the CPPs. Our data showed (Figure 7e) that Raji cells lacking the KCNQ5 potassium channel had a slightly decreased ability to bind TAT-RasGAP317-326 but importantly, these cells, at similar or even higher initial surface binding compared to wild-type cells (this was achieved by adequately varying the CPP concentrations), were still drastically impaired in taking up the peptide. Note that after one hour of incubation with TAT-RasGAP317-326 in the presence of serum there is only marginal amount of cell death (317-326, we have now performed an additional experiment with TAT that is not toxic to cells that confirms our data obtained with TAT-RasGAP317-326.

Page 9 {section sign} 3 and Page 10 {section sign} 1

Q14.The authors should have used a construct that does not kill the cells much earlier, just after the screening experiments based on resistance to necrosis induced by TAT-rasGAP. For Supp. Fig 8a and b: I am fully convinced by Raji cells and HeLa cells but not by the SKW6.4 cells.

A14. As mentioned in our answer to point 10, we agree that SKW6.4 cells present intermediate phenotypes probably because, unlike Raji and HeLa cells, a combination of ion channels seems to regulate the plasma membrane potential. As indicated above, we can move the SKW6.4 data to the supplementary information to clarify the message presented in the main text. Again, feedback from the editors is welcome here.

Page 10 {section sign} 2

Q15. A) Supp. Fig 9 is quite convincing but adds the information that 2 µM are sufficient in neurons. This again makes the 20 to 80 µM concentrations used on transformed cells unsatisfactory.

B) If one needs a cell line (more user friendly than primary cultures), there are several neural ones that can be differentiated (SHY, LHUMES, etc.) that may have an appropriate membrane potential (below -90mV). Indeed, it would then be important to verify if pore formation is still induced by TAT, R9 and Penetratin (separately) on "naturally" hyperpolarized cells.

C) Figure 2a confirms that changes in Vm are not solid for HeLa and SKW6.4 cells. This casts a doubt on the validity of the results obtained with the latter 2 cell lines.

A15. A) The experiments performed in Supplementary Fig. 9d with cortical rat neurons and HeLa cells were performed in the absence of serum accounting for the low concentrations used. We apologize for not emphasizing enough when experiments were performed in the presence or absence of serum, explaining the use of high CPP concentrations (40-80 mM) and low CPP concentrations (2-10 mM), respectively. We would like to emphasize however that we have adjusted the concentrations of CPPs in our study so as to get similar levels of CPP activity or CPP uptake between the different cell lines used. The concentrations used should not be compared as mere numbers, it is the CPP activity or uptake that should be considered.

B) We thank the reviewer for his/her suggestion. To address this point, we will perform a new experiment to determine if in neurons TAT, R9, and Penetratin induce pores (using the PI uptake approach).

C) Please see our answer to point 10.

Page 11 {section sign} 2

Q16. Why valinomycin was only tried on Raji cells?

A16. In this study, valinomycin was used on Raji and HeLa cells (Figure 2 and 3). We did not use valinomycin on SKW6.4 cells, as the drug-induced hyperpolarization levels were insufficient in this cell line. As we got a nice hyperpolarization in HeLa wild-type and KCNN4 KO cells through ectopic expression of the KCNJ2 potassium channels (which restored the ability of the KO cells to take up the CPPs), we did not perform the CPP uptake experiment with valinomycin in HeLa cells (although we had tested that valinomycin is able to hyperpolarize HeLa cells).

Page 12 {section sign} 2

Q17.A)Looking at Fig. 2c, it seems that low Vm increases the uptake of all CPPs, except Transportan. Is there any reason why this Figure does not provide the number of vesicles per cell in the hyperpolarized conditions?

B) In fact, if one goes to Supp. Fig. 9c, it appears that, among all peptides, only Penetratin is almost entirely cytoplasmic after 90' of incubation, whereas MAP and Transportan remain essentially vesicular. TAT and R9 are at mid-distance between these two extremes. This leads to send again the warning that all CPPs cannot be placed in a single category. The table that describes the sequences strongly suggests that, TAT and R9 uptake is due to the numerous Rs that cannot be replaced by Ks. In the case of Penetratin, that only has 3 Rs, the situation is thus different with the presence of 2 Ws previously shown to be mandatory for internalization, although absent in TAT ad R9.

C) In Supp. Fig9, panel g is useless.

D) A difference between peptides is also visible in Figure 2d where depolarization with KCl does not show the same efficiency on all peptides. The issue is whether these differences are significant and, if so, why? This discussion could be restricted to TAT, R9 and Penetratin.

E) Supp. Fig. 10a also suggests that all peptides do not respond similarly to depolarization and that the effects differ between cell types and concentrations used. However, given the high concentrations used and the high variance between replicates, this figure might not be a priority in the reorganization of the manuscript.

A17. A) As mentioned in the figure legend “Quantitation of vesicles was not performed in hyperpolarizing conditions due to masking from strong cytosolic signal.” This would create a bias towards underestimation of vesicles numbers in cells displaying strong cytosolic signal.

B) We agree with the reviewer that Transportan enters cells primarily through endocytosis. This is mentioned in the text as well as other differences that were observed with regards to the prevalence of endocytosis or direct translocation. These mentions are reported below.

Page 12: “With the notable exception of Transportan, depolarization led to decreased cytosolic fluorescence of all CPPs, while hyperpolarization favored CPP translocation in the cytosol (Fig. 2c, Supplementary Fig. 9h and 10a). Transportan, unlike the other tested CPPs, enters cells predominantly through endocytosis (Supplementary Fig. 9e), which could explain the difference in response to Vm modulation.”

Page 14: “Even though this extrapolation is likely to lack accuracy because of the well-known limitation of the MARTINI forcefield in describing the absolute kinetics of the molecular events, the values obtained are consistent with the kinetics of CPP direct translocation observed in living cells (Figure 1c and Supplementary Fig. 1b and 9e). With the exception of Transportan, the estimated CPP translocation occurred within minutes. This is consistent with our observation that Transportan enters cells predominantly through endocytosis and its internalization is therefore not affected by changes in Vm (Fig 2c-d and Supplemental Fig. 9e)”.

Page 20: “On the other hand, when endocytosis is the predominant type of entry, CPP cytosolic uptake will be less affected by both hyperpolarization and depolarization, which is what is observed for Transportan internalization in HeLa cells (Fig. 2c and Supplementary Fig. 10a).”

Concerning the roles of arginine and tryptophan residues, please refer to our answer #4.

C) We do not think this panel (now panel h) is useless as it shows representative examples of the quantitation shown in Figure 2c. We can however remove it if requested by the editors.

D) The reviewer is correct with the observation that KCl-induced depolarization does not lead to similar inhibition in uptake of the tested CPPs. As mentioned in the text, these differences can be explained by the prevalence of direct translocation in the cells. For example, transportan enters cells primarily through endocytosis, which as we show is not regulated/affected by the membrane potential (Figure 2c, lower graphs). Consequently, it is expected that KCl treatment will not impact on transportan cellular uptake.

E) The reviewer is correct in mentioning that there is quantitative heterogeneity between the different CPP tested. We mentioned these differences in the manuscript. These mentions are those that are reported under B, plus those listed below.

Page 19: “It is known for example that peptides made of 9 lysines (K9) poorly reaches the cytosol (Fig. 3f and Supplementary Fig. 9e) and that replacing arginine by lysine in Penetratin significantly diminishes its internalization10,11. According to our model, K9 should induce megapolarization and formation of water pores that should then allow their translocation into cells. However, it has been determined that, once embedded into membranes, lysine residues tend to lose protons12,13. This will thus dissipate the strong membrane potential required for the formation of water pores and leave the lysine-containing CPPs stuck within the phospholipids of the membrane. In contrast, arginine residues are not deprotonated in membranes and water pores can therefore be maintained allowing the arginine-rich CPPs to be taken up by cells.”

Page 21: “Therefore, the uptake kinetics of lysine-rich peptide, such as MAP, appears artefactually similar as the uptake kinetics of arginine-rich peptides such as R9 (Supplementary Fig. 11b).”

Page 21: “The differences between CPPs in terms of how efficiently direct translocation is modulated by the Vm (Fig. 2c-d and Supplementary Fig. 10a) could be explained by their relative dependence on direct translocation or endocytosis to penetrate cells. The more positively charged a CPP is, the more it will enter cells through direct translocation and consequently the more sensitive it will be to cell depolarization (Fig. 2c). On the other hand, when endocytosis is the predominant type of entry, CPP cytosolic uptake will be less affected by both hyperpolarization and depolarization, which is what is observed for Transportan internalization in HeLa cells (Fig. 2c and Supplementary Fig. 10a).”

However, what remains is that depolarization always affects CPP uptake, at most concentrations tested. The heterogeneity reported in Supplementary Fig. 10a for a given experimental condition in a given cell type is in itself of interest as it suggests that there are varying factors within a cell population (e.g. cell cycle, metabolism, etc.) that may impact on the ability of cells to take up CPPs. As per reviewer’s suggestion we may remove this panel from the figure if instructed to do so by the editors.

Page 12 {section sign} 3 and Page 13 {section sign} 1

Q18. The pH story is either too long or too short.

A18. One mechanism put forward to explain direct translocation relies on pH variation between the extracellular milieu and the cytosol14. It was therefore of interest in the context of the model we putting forward to see if pH is affecting the uptake of CPPs in our experimental model. Our data show that pH variations do not affect CPP direct translocation. This information should in our opinion be disclosed.

Page 14 {section sign} 2

Q19. At low Vm values, there is a decrease in free energy barrier. Does this modify temperature-dependency for internalization? Do cells really require energy when the Vm is very low, like is often the case for neurons?

A19. We thank the reviewer for this interesting comment. We will now address this by visualizing under a confocal microscope CPP direct translocation in rat cortical neurons incubated at various temperature (4°C, 24°C, 37°C).

Page 15 {section sign} 2

Q20. Figure 2e is not explained, not even in the legend while the statement that CPPs induce a local hyperpolarization is central to the study.

A20. As there is no Figure 2e, we believe that the reviewer is talking about Figure 3e, the legend of which was present in the initial version of the manuscript.

Page 16 {section sign} 1

Q21. It is confusing that the same agent, here PI, is used to measure internalization (2 nm pore formation in response to hyperpolarization,) and cell death. I have seen the explanation below, but I do not find it fully satisfactory.

A21. We have tried to explain this better under our answer to point 11B.

Page 16 {section sign} 2

Q22. Entry is not necessarily a size issue. Structure is an important parameter, including possible structure changes, for example in response to Vm modifications. Therefore, the statement that molecule with larger diameters are mostly prevented from internalization is not only vague ("mostly") but incorrect.

A22. We agree with the reviewer’s comment in the sense that the secondary structure of a molecule will also play an important role in its internalization. For that reason, we have used a series of molecules of identical structure (dextrans) but that have different molecular weights. In these experiments we saw that dextran of higher molecular weight enter less efficiently than that of lower molecular weight (Figure 3). We will rephrase some of our sentences so to precise that the size and the shape (structure) of molecules will determine their ability to enter cells through water pores that are characterized by a certain diameter.

Page 2: “Using dyes of varying sizes and shapes, we assessed the diameter of the water pores**.”

Page 4: “translocation and we characterize the diameter of the water pores used by CPPs**.”

Page 15: “cells were co-incubated with molecules of different sizes and structure and FITC-labelled CPPs at a peptide/lipid ratio of 0.012-0.018 (Supplementary Fig. 11c-d).”

Page 16: “3 kDa, 10 kDa, and 40 kDa dextrans, 2.3 ±0.38 nm, 4.5 nm and 8.6 nm (diameter estimation provided by Thermofisher), respectively, were used to estimate the diameter of the water pores formed in the presence of CPP.”

Page 16: “These results are in line with the in silico prediction of the water pore diameter obtained by analyzing the structure of the pore at the transition state.”

Page 16: “The marginal cytosolic co-internalization of dextrans was inversely correlated with their diameter.”

Page 35: “200 µg/ml dextran of different molecular weight in the presence or in the absence of the indicated CPPs in normal […]”.

Page 17 {section sign} 4 and Page 18 {section sign} 1

Q23. In Supp. Fig. 13b and c, since the GAP domain is mutated, death is not due to RasGAP activity. So what causes zebrafish death (hyperpolarization?) The results seem contradictory with those of Supp. Fig 13f where survival is 100% at 48 h.

A23. Indeed, it appears that valinomycin in water leads to zebrafish embryo death, as can be seen in Supplementary Fig. 13c. However, the main difference between Supplementary Fig. 13c and S13f is that in Supplementary Fig. 13f zebrafish were not incubated in valinomycin-containing water, but were locally injected with a CPP in the presence or in the absence of valinomycin. This has now been clarified in the text. We saw that local injections with the hyperpolarizing agent are much less toxic and are well tolerated by the zebrafish embryos.

Page 18 {section sign} 2

Q24. The formation of inverted micelles is not incompatible with that of pores. CPP-induced hyperpolarization (Vm) is not measured directly, but deduced from experiments involving artificial membranes and in silico modeling. It would be useful to distinguish between what takes place on live cells (in vitro and in vivo) and what is speculated (based on modeling and artificial systems).

A24.

The formation of inverted micelles is not incompatible with that of pores.

As mentioned above (point 9), we do also think that what has been presented as inverted micelles could have been in fact water pores.

CPP-induced hyperpolarization (Vm) is not measured directly, but deduced from experiments involving artificial membranes and in silico modeling. It would be useful to distinguish between what takes place on live cells (in vitro and in vivo) and what is speculated (based on modeling and artificial systems).

If we understand this point correctly, the reviewer is talking about the -150 mV hyperpolarization. This value is not a speculation but has been estimated from in silico experiments and also from experiments using live cells (not artificial membranes). In living cells, the hyperpolarization (megapolarization) has been estimated based on accumulation of intracellular PI over time in the presence or in the absence of CPP.

Page 19 {section sign} 3

Q25A. The model posits that the number of Rs influences the ability of the CPPs to hyperpolarize the membrane and, consequently, to induce pore formation. Since pore formation is key to the addressing to the cytoplasm, how can one explain that Penetratin which has only 3 Rs is transported to the cytoplasm more readily that TAT or R9? The authors should take this contradiction in consideration and should not leave aside, in the literature, what does not fit with their model.

A25A. We fully agree that this should be discussed and not left aside. Please refer to point 4 for detailed discussion about the role of arginine and tryptophan in the ability of CPPs to translocate across membranes.

Q25B. The fact that that Rs cannot be replaced by Ks, both in R9 and Penetratin is explained by differences in deprotonization. This is interesting but speculative. It might be that the interaction between Rs versus Ks with lipids and sugars are different and not only based on charge. After all their atomic structures, beyond charges, are different.

A25B. We do not claim that protonation differences between R and K is the definitive answer for their ability to promote CPP translocation. It is one possible explanation that we find sound. As suggested by the reviewer, the ability of K and R to bind lipids and sugars can also play a role. We can mention in this context that the guanidinium group of arginine residues can form two hydrogen bonds1, which allow for more stable electrostatic interactions while the lysyl group of lysine residues can only form one hydrogen bond. We have included these additional possibilities in the revised version of our manuscript as indicated under point 4.

Page 20 {section sign} 1 Q26. We still need to understand endosomal escape.

A26. We agree with the reviewer that endosomal escape is still poorly understood. This is an interesting research topic that deserves its own separate study.

**Major comments**

• The key conclusions are convincing for a subset of CPPs and cell types
• Yes, some claims should be qualified as speculative, but not preliminary
• Many experiments should be removed. Neuronal primary cultures should be introduced to verify the main conclusions, at least for the 3 mains CPPs (TAT, R9, Penetratin). Answers must be given to the concentration issue. Vesicles should be characterized as well as the localization of the peptides in or around the vesicles. See above for less decisive but still important experiments that would benefit to the study.
• Yes, the requested experiments correspond to a reasonable costs and amount of time (10 to 20,000 € and 3 to 5 months of work)
• Yes, the methods are presented with great details. -Yes, the experiments are adequately replicated and statistical analysis is adequate

**Minor comments (not so minor for some of them)**

• See "Detailed analysis"
• No, prior studies are not referenced appropriately (see above)
• No, the text and figures are not clear and not accurate (see above)
• (i) use Raji cells and primary neuronal cultures, plus in vivo model and forget the other cell types; (ii) forget MAP and Transportan and compare TAT/R9 and Penetratin; (iii) drastically reduce the number of figures, tables and movies (6 primary figures, 6 supplemental figures and 4 tables are reasonable numbers; movies are not absolutely necessary); (iv) limit to 6 (max) the number of panels per figure; (v) limit the number of references to less than 50 and cite the primary reports rather than reviews); (vi) reduce the size of the Material and Methods and the length of figure legends.

Reviewer #1 (Significance (Required)):

• The mode of CPP internalization is an unanswered question and the report, if revised, will represent a conceptual and technical advance.
• Bits and pieces of the conclusions can be found in previous reports. But the Vm-dependent pore formation as well as the CPP-induced "megapolarization" (even if only shown for a subset of CPPs) would be an important contribution. The authors must resist the tentation to generalize to all CPPs what might only be true for a few of them.
• I do not have the expertise for the in-silico work, but my field of expertise allows me to understand all other aspects of the manuscript.

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

In this manuscript, the authors investigated the effect of membrane potential on the internalization of CPPs into the cytosol of some cancer cell lines. Using a CRISPR/Cas9-based screening, they found that some potassium channels play an important role in the internalization of CPPs. The depolarization decreases the rate of internalization of CPPs and the hyperpolarization using valinomycin increases the rate. Using the coarse-grained MD simulations, the authors investigated the interaction of CPPs with a lipid bilayer in the presence of membrane potential. In the interaction of CPPs with the cells, propidium iodide (PI) enters the cytosol significantly. Based on this result, the authors concluded that pores with 2 nm diameter are formed in the plasma membrane.

This reviewer raises one main issue concerning CPP endocytosis. The reviewer challenges our method to investigate CPP direct translocation and specifically how do we make sure that what we consider direct translocation is not a combination of CPP endocytosis (followed or not by endosomal escape) and CPP plasma membrane translocation. As explained below in details our methodology is able to accurately distinguish CPP uptake by direct translocation from CPP endocytosis and we further demonstrate that endosomal escape does not occur in our experimental settings.

Q27. One of the defects in this manuscript is the method to determine the fraction of internalization of CPPs via direct translocation across plasma membrane. The authors estimated the fraction of the direct translocation of CPPs by the fluorescence intensity of the cytosolic region (devoid of endosomes) and the fraction of the internalization via endocytosis by the fluorescence intensity of vesicles. However, the CPPs can enter the cytoplasm via endocytosis, and thus the increase in the fluorescence intensity of the cytoplasm is due to two processes (via endocytosis and direct translocation). The authors should use inhibitors of clathrin-mediated endocytosis and macropinocytosis to determine the fraction of internalization of CPPs via direct translocation accurately. Low temperature (4 C) has been also used as the inhibitor of endocytosis (e.g., J. Biophysics, 414729, 2011; J. Biol. Chem., 284, 33957, 2009). Supplementary Figure 1i (the temperature dependence of internalization of TAT-RasGAP317-326) clearly shows that at 4 C the fraction of the internalization was very low, indicating that this peptide enters the cytosol mainly via endocytosis. The determination of the fraction of the internalization via endocytosis by the fluorescence intensity of vesicles in this manuscript is not accurate because it is difficult to examine all endosomes in cells and it is not easy to discriminate the fluorescence intensity due to the endosomes from that due to the cytosol.

It is important to follow a time course of the fluorescence intensity of single cells from the beginning of the interaction of CPPs with the cells (at least from 5 min) in the presence and absence of inhibitors of the endocytosis (J. Biol. Chem., 278, 585, 2003) to elucidate the process of the internalization of CPPs in the cytosol.

A27. The reviewer raises the possibility that the signal of fluorescent CPPs in endosomes somehow perturbs the acquisition of the signal in cytosol. This could occur in two ways: CPP endosomal escape and diffusion of the signal located in endosomes into adjacent cytosolic regions (halo effect). The second possibility can be readily dismissed because in situations where cells only take up fluorescent CPPs by endocytosis, the cytosol emits background fluorescence (autofluorescence). This can be seen in Supplementary Fig. 1a (“vesicular” condition) or in Supplementary Fig. 9h in the depolarized cells that cannot take up CPP by direct translocation. Also note that when we record the cytosolic signal we take great care of using regions of interest (ROI) that are distant from endosomes. In contrast to what the reviewer is saying (“it is not easy to discriminate the fluorescence intensity due to the endosomes from that due to the cytosol”), it is actually not difficult discriminating the cytosolic fluorescence from the endosome fluorescence. To illustrate this, we now provide examples of high magnification images of cells incubated with fluorescent CPPs (new Supplementary Fig. 1c, right[1]) to better explain/illustrate our methodology and to show that it is quite straightforward to find cytosolic areas devoid of endosomes. Such high magnification images are those that are used for our blinded quantitation. The other possibility is endosomal escape. We demonstrate in Supplementary Fig. 7c that in our experimental conditions, no endosomal escape is detected[2]. We may not have explained our methodology well enough in the earlier version. We will try and improve the description of our quantitation procedures better in the revised version. To this end, we have now added a scheme illustrating the experimental setup (now part of Supplementary Fig. 7c) that is used to assess endosomal escape.

The reviewer also questions the way we quantitate the CPP signals in endosomes. In the present paper, our goal is to characterize the direct translocation process of CPPs in to cells. We do not wish here to investigate in details the endocytic pathway taken by CPPs. This has been done in a separate study that we are currently submitting for publication. In a nutshell, this work shows that the endocytic pathway taken by CPPs is different from the classical Rab5- and Rab7-dependent pathway and that the CPP endocytic pathway is not inhibited by compounds that affect the classical pathway. Thus, even if we had wanted to use the inhibitors mentioned by the reviewer, they would not have blocked CPP endocytosis.

To sum up the issues raised under this point, we believe we have presented the reasons why there are no grounds to support the concerns raised by the reviewer.

[1] Supplementary Fig. 1c (right) is mentioned in the “Cell death and CPP internalization measurements” section of the methods.

[2] In this experiment, cells were incubated with CPPs for 30 minutes to allow CPP entry into cells. Then the cells were either washed (to prevent further uptake including uptake through direct translocation) or incubated in the continued presence of CPPs. In both conditions, cells where only endocytosis took place were followed by time-lapse confocal microscopy for 4 hours (i.e. these cells do not display any cytosolic CPP signal at the beginning of the recording). We then assessed the CPP fluorescence intensity within the cytosol (i.e. away from endosomes). From these experiments we saw that cytosolic fluorescence increased only in conditions where CPP was present in the media throughout the experiment. No increase of cytosolic fluorescence was detected in the condition where CPPs were washed out. In conclusion these results demonstrate that the cytosolic signal that we observed in our experiments is due to direct translocation and not endosomal escape. In these experiments we have used the LLOME lysosomotropic agent as a control to make sure that if endosomal escape had occurred (even if only from a subset of endosomes/lysosomes), we would have been able to detect it. Indeed, upon addition of LLOME we were able to record CPP release from endosomes to the cytosol. There is therefore no endosomal escape occurring in our experimental conditions. In conclusion, the observed cytosolic signal in our confocal experiments do not originate, even partly, from endosomal escape.

Supplementary Figure 1i (the temperature dependence of internalization of TAT-RasGAP317-326) clearly shows that at 4 C the fraction of the internalization was very low, indicating that this peptide enters the cytosol mainly via endocytosis.

The experiment shown in Supplementary Fig. 1i was analyzed by flow cytometry that cannot discriminate the cytosolic signal from the endosomal signal. We will therefore perform this experiment again but this time using confocal imaging to record the impact of temperature on CPP cytosolic acquisition. We have performed this for HeLa cells already and this shows that direct translocation is indeed inhibited by low temperatures (full blockage at 4°C). Bear in mind that no endosomal escape occurs in our settings (see Supplementary Fig. 7c). This indicates that the decrease in cytoplasmic fluorescence induced by low temperature is not a consequence of diminished CPP endocytosis.

Q28. Recently, it has been well recognized that membrane potential greatly affects the structure, dynamics and function of plasma membranes (e.g., Science, 349, 873, 2015; PNAS, 107, 12281, 2010). The results of the effect of membrane potential on the internalization of CPPs (depolarization decreases the rate of internalization and hyperpolarization increases the rate), which is main results of this manuscript, can be interpreted by various ways. For example, the rate of endocytosis may be greatly controlled by membrane potential, which can explain the authors' results.

A28. This reviewer may have missed the experiment presented in Figure 2c that clearly shows that CPP endocytosis is unaffected by depolarization or hyperpolarization of cells. We have also determined that transferrin uptake through endocytosis is not affected by potassium channel knockout (which also leads to depolarization). The possibility raised by the reviewer is therefore refuted by our experimental evidence.

Q29. A) The authors used the similar concentrations of various CPPs for their experiments (10 to 40 microM), and did not examine the peptide concentration dependence of the internalization. It has been recognized that the CPP concentration affects the mode of internalization of CPPs (e.g., J. Biol. Chem., 284, 33957, 2009). The authors should examine the peptide concentration dependence of the mode of internalization (less than 10 micorM, e. g., 1 microM).

B) In the case of depolarization, can higher concentrations of CPPs (e.g., 100 micorM) induce their internalization?

A29. A) We agree that CPPs/cell ratio might prompt one mode of entry over the other. It has been reported by imaging that at lower CPP concentrations endocytosis is favored since only vesicles were observed15-19. Our data confirm this (new Supplementary Fig. 9f).

B) In Supp. Fig. 7e we have incubated KCNQ5 KO Raji cells that are slightly more depolarized than WT cells in the presence of increasing CPP concentrations up to 100 m From the obtained results, we can see that at 100 mM, the uptake in depolarized cells is increased but does not reach the level of uptake seen in wild-type cells. Therefore, lack of hyperpolarization can be compensated to a mild extent by increased CPP availability.

Q30. A) The effects of membrane potential on plasma membranes and lipid bilayers have been extensively investigated experimentally and thus are well understood, although currently the coarse-grained MD simulations cannot provide quantitative results which can be compared with experimental results. In this manuscript, using the coarse-grained MD simulations, the authors applied 2.2 V to a lipid bilayer to examine the translocation of CPPs. However, it is well known the experimental results that application of such large voltage to a lipid bilayer induces pore formation in the membrane or its rupture (Bioelectrochem. Bioenerg., 41, 135, 1996; Sci. Rep., 7, 12509, 2017), but at low membrane potential (B) What is the probability of the existence of R9 in the surface of the membrane? R9 cannot bind to the electrically neutral lipid bilayers (such as PC) under a physiological ion concentration (Biochemistry, 55, 4154, 2016). Even if in the case of R9 the membrane potential reaches at -150 mV, the other CPPs have lower surface charge density than that of R9, and hence, the decrement of membrane potential is lower. The authors should provide the data of other CPPs.

C) It has been reported that the negative membrane potential increases the rate of entry of two kinds of CPPs into the lumen of giant unilamellar vesicles (GUVs) without leakage of water-soluble fluorescent probe (Stokes-Einstein radius; ~0.9 nm diameter), i.e., no pore formation in the GUV membrane (Biophys., 118, 57, 2020, J. Bacteriology, 2021, DOI: 10.1128/JB.00021-21). The authors should discuss the similarity and the difference between the results in these papers and the above results in this manuscript.

A30. A) As correctly stated by this Reviewer, we reported simulations with high transmembrane potential values, which is a common procedure in in silico simulations used to accelerate the kinetics of the studied process. In this manuscript we have additionally developed and carefully validated a novel protocol to estimate the free energy landscape of water pore formation and CPP translocation under physiological transmembrane potential (further details about the methodological procedure, the convergence and the validation of the free energy estimation are reported in Supplementary Fig. 15-19 of the manuscript). This protocol allowed us to demonstrate the impact of megapolarization (‑150 mV) on the free energy barrier corresponding to the CPP translocation process. The results exemplify how the megapolarization process modifies the uptake probability of the R9 peptide, reducing locally the free energy barrier of the membrane translocation (Fig. 3c-d). Moreover, we have also demonstrated how a single CPP produces a local transmembrane potential of about -150 mV, in agreement with our hypothesis (Fig. 3e).

Finally, the quantitative accuracy of the molecular simulations was found to be satisfactory because the water pore formation free energy in a symmetric DOPC membrane that we calculated is in excellent agreement with previous atomistic estimation (Table S5).

B) It has been demonstrated that CPP/membrane interactions are mostly electrostatic between positively charged amino acids carried by the CPPs and various negatively charged cell membrane components, such as glycosaminoglycans20-31 and phosphate groups32. It is in line with our model that the more positively charged CPPs are the better they should translocate into cells. Therefore, we agree with the reviewer that the level of megapolarization may vary according to the charges carried by the CPPs. However, our data clearly indicate that a certain membrane potential hyperpolarization threshold must be achieved to induce water pore formation. As suggested by the reviewer we will now conduct additional modeling experiments with other CPPs.

C) We have carefully read these papers and do not necessarily reach the same conclusions as the authors. In both papers, the translocation of CPPs in polarized GUVs is monitored through CPP acquisition on vesicles found within the GUVs (intraluminal vesicles; either smaller GUVs or LUVs). There is actually no evidence of the presence of luminal CPPs outside of the intraluminal vesicle membranes. We would therefore argue that these studies elegantly demonstrate that membrane potential increases CPP binding and insertion into the membrane of the mother GUVs but that the CPPs then move, by diffusion, from the lipidic boundary of the mother GUVs to the lipidic membranes of its intraluminal vesicles. This CPP diffusion would presumable occur when the intraluminal vesicles touch the outer membrane bilayer of the mother GUV. There is a marked lag between binding of the CPPs to the membrane of the mother GUV and appearance of CPPs on the intraluminal vesicles (Figure 3c of the Biophysical Journal paper). This lag is, according to us, more compatible with the explanation we are giving than with a translocation mechanism. If there were direct translocation of the CPP through the membrane of the mother GUV, such a large lag would not be expected to be seen (see next point). If there is no translocation of the CPPs across the GUV membrane, it could explain why the water soluble dye within the mother GUVs does not leak out.

Q31. The authors consider that the translocation of CPPs induces depolarization, and as a result, the pore closes immediately. This kind of transient pore cannot explain the authors' result of the significant entry of PI into the cytosol during the interaction of CPPs with the cells. The authors should explain this point.

A31. Our interpretation is that PI takes advantage of the water pore triggered by hyperpolarization to penetrate cells. PI is positively charged and is attracted by the negative membrane potential of the cells. Its movement across the cell membrane is therefore unidirectional. This enables the PI molecules to accumulate/concentrate within the cytosol (Supplementary Fig. 12). When PI is in the presence of a CPP, both molecules enter with similar kinetics (Supplementary Fig. 12a and the new quantitation provided in the partially revised version of the manuscript; Supplementary Fig. 12b). PI and CPPs do no interact (Supplementary Figure 12d); hence they move independently from one another.

Q32. In this manuscript, the authors used only cancer cell lines (Raji cell, SKW6.4 cell, and HeLa cell). The lipid compositions and the stability of the plasma membranes of these cells may be different from normal cells (e.g., 33; Cancer Res., 51, 3062, 1991). Is there a possibility that negatively charged lipids such as PS and PIP2 locate in the outer leaflet locally in these cells? At least, some discussions on this point is essential.

A32. We agree with the reviewer that plasma membrane composition may vary between cancerous and not cancerous cells and that this may impact on the ability of CPPs to cross cellular membranes. We now mention this in the discussion: “While the nature of the CPPs likely dictate their uptake efficiency as discussed in the precedent paragraph, the composition of the plasma membrane could also modulate how CPPs translocate into cells. In the present work, we have recorded CPP direct translocation in transformed or cancerous cell lines as well as in primary cells. These cells display various abilities to take up CPPs by direct translocation and the present work indicates that this is modulated by their Vm. But as cancer cells display abnormal plasma membrane composition33, it will be of interest in the future to determine how important this is on their capacity to take up CPPs”.

Q33. The authors found that PI enters the cytosol significantly when CPPs interact with these cells. Based on this result, the authors concluded that pores with 2 nm diameter are formed in the plasma membrane. However, they did not show the time courses of entry of PI and that of CPPs, and thus we cannot judge whether the pore formation in the plasma membrane is the cause of the entry of CPPs or the result of the entry of CPPs. We can reasonably consider that CPPs enters the cytosol via endocytosis and bind to the inner leaflet of the plasma membrane, inducing pore formation in the plasma membrane.

A33. The kinetics we are now showing in point A31 indicate co-entry of CPPs and PI, an observation that is in line with our model. Also note that we have demonstrated that CPPs do not escape endosomes (please see our answers to questions 12 and 28). These data are therefore not compatible with the reviewer’s interpretation.

Q34. It has been reported that the negative membrane potential increases the rate constant of antimicrobial peptide (AMP)-induced pore formation or local damage in the GUV membrane (J. Biol. Chem., 294, 10449, 2019; BBA-Biomembranes, 1862, 183381, 2020). These results are related to those in the present manuscript, because here the authors consider that CPPs induce pores in the plasma membrane in the presence of negative membrane potential.

A34. We thank the reviewer for mentioning these interesting articles. As we understand them, they demonstrate that antimicrobial peptides (AMPs) bind membranes better as a function of increasing negative membrane potential and that this favors their ability to form pores in the membrane, compromising membrane integrity and inducing the release of cytosolic or luminal content. These AMPs do not behave exactly like CPPs because the latter do not compromise the integrity of the membranes.

In conclusion, the results of the membrane potential dependence of the rate of the internalization of CPPs may be solid results, which is an important contribution. However, the other analyses and the interpretations are not conclusive at the current stage.

We thank the reviewer for the positive assessment of our results concerning the membrane potential dependence on CPP uptake. Hopefully we have clarified the remaining points with our answers developed above and with the new data we are presenting.

Reviewer #2 (Significance (Required)):

(1) Using a CRISPR/Cas9-based screening, the authors found that some potassium channels play an important role in the internalization of CPP TAT-RasGAP317-326. This result advances the field of CPPs.

(2) Several researches have suggested that the depolarization decreases the rate of internalization of CPPs into cell cytosol and the hyperpolarization increases the rate. It has been also reported that negative membrane potential increases the rate of entry of two kinds of CPPs into the lumen of GUVs of lipid bilayers. The authors provide a new genetic evidence that membrane potential plays an important role in the internalization of CPPs in the cytosol. However, modulation of membrane potential affects the structure, dynamics and function of plasma membranes greatly. At the current stage, it is difficult to judge which process of the internalization of CPPs is affected by the membrane potential.

(3) The researchers of CPPs and AMPs are interested in their results after they improve the contents of the manuscript.

(4) My field of expertise is membrane biophysics, especially the interaction of AMPs and CPPs with GUVs and cells.

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, the authors investigated the effect of membrane potential on the internalization of CPPs into the cytosol of some cancer cell lines. Using a CRISPR/Cas9-based screening, they found that some potassium channels play an important role in the internalization of CPPs. The depolarization decreases the rate of internalization of CPPs and the hyperpolarization using valinomycin increases the rate. Using the coarse-grained MD simulations, the authors investigated the interaction of CPPs with a lipid bilayer in the presence of membrane potential. In the interaction of CPPs with the cells, propidium iodide (PI) enters the cytosol significantly. Based on this result, the authors concluded that pores with 2 nm diameter are formed in the plasma membrane.

One of the defects in this manuscript is the method to determine the fraction of internalization of CPPs via direct translocation across plasma membrane. The authors estimated the fraction of the direct translocation of CPPs by the fluorescence intensity of the cytosolic region (devoid of endosomes) and the fraction of the internalization via endocytosis by the fluorescence intensity of vesicles. However, the CPPs can enter the cytoplasm via endocytosis, and thus the increase in the fluorescence intensity of the cytoplasm is due to two processes (via endocytosis and direct translocation). The authors should use inhibitors of clathrin-mediated endocytosis and macropinocytosis to determine the fraction of internalization of CPPs via direct translocation accurately. Low temperature (4 C) has been also used as the inhibitor of endocytosis (e.g., J. Biophysics, 414729, 2011; J. Biol. Chem., 284, 33957, 2009). Supplementary Figure 1i (the temperature dependence of internalization of TAT-RasGAP317-326) clearly shows that at 4 C the fraction of the internalization was very low, indicating that this peptide enters the cytosol mainly via endocytosis. The determination of the fraction of the internalization via endocytosis by the fluorescence intensity of vesicles in this manuscript is not accurate because it is difficult to examine all endosomes in cells and it is not easy to discriminate the fluorescence intensity due to the endosomes from that due to the cytosol.

It is important to follow a time course of the fluorescence intensity of single cells from the beginning of the interaction of CPPs with the cells (at least from 5 min) in the presence and absence of inhibitors of the endocytosis (J. Biol. Chem., 278, 585, 2003) to elucidate the process of the internalization of CPPs in the cytosol

Recently, it has been well recognized that membrane potential greatly affects the structure, dynamics and function of plasma membranes (e.g., Science, 349, 873, 2015; PNAS, 107, 12281, 2010). The results of the effect of membrane potential on the internalization of CPPs (depolarization decreases the rate of internalization and hyperpolarization increases the rate), which is main results of this manuscript, can be interpreted by various ways. For example, the rate of endocytosis may be greatly controlled by membrane potential, which can explain the authors' results.

The authors used the similar concentrations of various CPPs for their experiments (10 to 40 microM), and did not examine the peptide concentration dependence of the internalization. It has been recognized that the CPP concentration affects the mode of internalization of CPPs (e.g., J. Biol. Chem., 284, 33957, 2009). The authors should examine the peptide concentration dependence of the mode of internalization (less than 10 micorM, e. g., 1 microM). In the case of depolarization, can higher concentrations of CPPs (e.g., 100 micorM) induce their internalization? The effects of membrane potential on plasma membranes and lipid bilayers have been extensively investigated experimentally and thus are well understood, although currently the coarse-grained MD simulations cannot provide quantitative results which can be compared with experimental results. In this manuscript, using the coarse-grained MD simulations, the authors applied 2.2 V to a lipid bilayer to examine the translocation of CPPs. However, it is well known the experimental results that application of such large voltage to a lipid bilayer induces pore formation in the membrane or its rupture (Bioelectrochem. Bioenerg., 41, 135, 1996; Sci. Rep., 7, 12509, 2017), but at low membrane potential (< ~200 mV) a lipid bilayer is stable although they have transient pre-pores (Biophys. J., 85, 2342, 2003; Biophys. J., 80, 1829, 2001). In the main results obtained in the experiments of cells in this manuscript, the values of the membrane potential are less than -100 mV. Therefore, this description of their results of MD simulations is misleading. According to their theory, only at much lower Vm values (-150 mV) induces a large decrease in free energy barrier of the translocation of CPPs across the lipid bilayer. Is this due to the pore formation in the membrane? The description of this point is poor, and thus it is diffiult to understand it. The authors consider that normal membrane potential is much higher than -150 mV, and thus the binding of positively charged CPPs in the membrane surface must increase the negative membrane potential to decrease the free energy barrier. Then, the authors suggest that the presence of R9 in contact with lipid membrane decreases the transmembrane potential to -150 mV according to the MD calculation. What is the probability of the existence of R9 in the surface of the membrane? R9 cannot bind to the electrically neutral lipid bilayers (such as PC) under a physiological ion concentration (Biochemistry, 55, 4154, 2016). Even if in the case of R9 the membrane potential reaches at -150 mV, the other CPPs have lower surface charge density than that of R9, and hence, the decrement of membrane potential is lower. The authors should provide the data of other CPPs. It has been reported that the negative membrane potential increases the rate of entry of two kinds of CPPs into the lumen of giant unilamellar vesicles (GUVs) without leakage of water-soluble fluorescent probe (Stokes-Einstein radius; ~0.9 nm diameter), i.e., no pore formation in the GUV membrane (Biophys., 118, 57, 2020, J. Bacteriology, 2021, DOI: 10.1128/JB.00021-21). The authors should discuss the similarity and the difference between the results in these papers and the above results in this manuscript.

The authors consider that the translocation of CPPs induces depolarization, and as a result, the pore closes immediately. This kind of transient pore cannot explain the authors' result of the significant entry of PI into the cytosol during the interaction of CPPs with the cells. The authors should explain this point.

In this manuscript, the authors used only cancer cell lines (Raji cell, SKW6.4 cell, and HeLa cell). The lipid compositions and the stability of the plasma membranes of these cells may be different from normal cells (e.g., J. Bioenergetics Biomem., 52, 321, 2020; Cancer Res., 51, 3062, 1991). Is there a possibility that negatively charged lipids such as PS and PIP2 locate in the outer leaflet locally in these cells? At least, some discussions on this point is essential.

The authors found that PI enters the cytosol significantly when CPPs interact with these cells. Based on this result, the authors concluded that pores with 2 nm diameter are formed in the plasma membrane. However, they did not show the time courses of entry of PI and that of CPPs, and thus we cannot judge whether the pore formation in the plasma membrane is the cause of the entry of CPPs or the result of the entry of CPPs. We can reasonably consider that CPPs enters the cytosol via endocytosis and bind to the inner leaflet of the plasma membrane, inducing pore formation in the plasma membrane.

It has been reported that the negative membrane potential increases the rate constant of antimicrobial peptide (AMP)-induced pore formation or local damage in the GUV membrane (J. Biol. Chem., 294, 10449, 2019; BBA-Biomembranes, 1862, 183381, 2020). These results are related to those in the present manuscript, because here the authors consider that CPPs induce pores in the plasma membrane in the presence of negative membrane potential.

In conclusion, the results of the membrane potential dependence of the rate of the internalization of CPPs may be solid results, which is an important contribution. However, the other analyses and the interpretations are not conclusive at the current stage.

Significance

(1) Using a CRISPR/Cas9-based screening, the authors found that some potassium channels play an important role in the internalization of CPP TAT-RasGAP317-326. This result advances the field of CPPs.

(2) Several researches have suggessted that the depolarization decreases the rate of internalization of CPPs into cell cytosol and the hyperpolarization increases the rate. It has been also reported that negative membrane potential increases the rate of entry of two kinds of CPPs into the lumen of GUVs of lipid bilayers. The authors provide a new genetic evidence that membrane potential plays an important role in the internalization of CPPs in the cytosol. However, modulation of membrane potential affects the structure, dynamics and function of plasma membranes greatly. At the current stage, it is difficult to judge which process of the internalization of CPPs is affected by the membrane potential.

(3) The researchers of CPPs and AMPs are interested in their results after they improve the contents of the manuscript.

(4) My field of expertise is membrane biophysics, especially the interaction of AMPs and CPPs with GUVs and cells.

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Referee #1

Evidence, reproducibility and clarity

Summary

The authors propose a mechanism through which voltage dependent water pore formation is key to the internalization of Cell permeable peptides (CPPs). The claim is based on an in-silico study and on several experimental approaches. The authors compare 5 peptides (R9, TAT-48-57, Penetratin, MAP and Transportan and use 3 distinct cell lines (Raji, SKW6.4 and HeLa cells), plus neurons in primary cultures. The also present in vivo experiment (mouse skin and zebrafish embryo). All in all, it is an interesting study, but it raises several issues that need to be addressed. Moreover, the length and structure of the manuscript make it very difficult to read (see below under "Reviewer statement")

Reviewer statement

The instructions are to use the "Major comments" section to answer 6 precise questions. Unfortunately, this is not possible due to the structure of the document to review. The main manuscript (22 pages) comes with 4 primary figures and 19 supplemental ones. Most of these figures have an enormous number of panels and their legends occupy 17 pages. To this, are added 6 supplemental tables and 7 supplemental movies (with 2 pages of legends), 28 pages of Material and Methods, and 146 References (109 for the main manuscript and 37 for Supplemental information). To be frank, I was often tempted to send the manuscript back, asking for the authors to submit a document facilitating the task of the reviewers.

Because of this complexity, my "Major comments" will come after a page by page, paragraph ({section sign}) by paragraph and figure by figure "Detailed analysis" of the manuscript.

Detailed analysis

Page 4 {section sign} 3 The test is based on the ability of TAT-RasGAP to kill the cells. Although controls exist, this is worrying since necrotic death might participate in the rupture of the membrane and artificially amplify internalization after a first physiological entry of the peptide. It is also a bit dangerous to add a FITC group to a short peptide without controlling that it has no effect on the interaction with the membrane (FITC-induced local hydrophobicity can provoke peptide tilting and membrane shearing). In the same vein, the very high peptide concentrations often used in the study (40µM for Raji and SKW6.4 cells and 80µM on HeLa cells) can be highly toxic.

Page 5 {section sign} 1 Supp. Fig.1a shows no differences between the 3 cell types, even though they differ in their modes of peptide internalization, some favoring vesicular staining and others cytoplasmic diffusion. Multiplying cell and peptide types contributes to the complexity of the manuscript without increasing its interest. If there is a conceptual breakthrough, as might be the case, it is obscured by the accumulation of useless images and data. A step into simplifying the manuscript would be (i), to concentrate on Raji cells (leaving out SKW6.4 and HeLa cells) and (ii) to only discuss the R9, TAT (including TAT-RasGAP) and Penetratin peptides. TAT and R9 are poly-R peptides, which is not the case for Penetratin that has only 3 Rs. These 3 Rs are important (cannot be replaced by 3 Ks), but the two Ws absent in R9 and TAT are equally important as they cannot be replaced by Fs. This must be considered by the authors when they tend to generalize their model. Supp. Fig1c-d is not necessary (very little information in it) and Supp. Fig 1e is misleading as it takes a lot of imagination to see a difference between homogenous (top) and focal (bottom) diffusion. Supp. Fig.1g: How many cells are we looking at? Given the high variance, the result cannot be interpreted easily. A distribution according to fluorescence bits would be a better way to present the data.

Supp. Fig2i. This panel confirms that Raji cells differ from the two other cell types by showing clear temperature dependency. The explanation will come later with the energy barrier for low Vm-induced pore formation. This contradicts earlier reports showing that Penetratin translocation is not temperature-dependent, possibly because it was done on neurons naturally hyperpolarized. Or else because mechanisms are, at least in part, different from the one proposed here for R9 and TAT. This requires some clarification and supports the suggestion that, instead of multiplying models and peptides, it would be more efficient to compare TAT, R9 and Penetratin internalization by Raji cells and primary neurons. Supp. Fig. 2a-f. Last sentence of the legend "Concentrations above 40µM led to too extensive cell death preventing analysis of peptide internalization". This confirms the warning against the use of concentrations varying between 40µM and 80µ and partially jeopardizes the validity of some experiments.

Page 6 {section sign} 2 The authors advocate 2 modes of entry, opposing transport across the membrane and endocytosis. In contrast with R9, TAT and Penetratin, Transportan or MAP seem to be purely endocytosed but, if they reach the cytoplasm, they still have to cross a membrane (unless "a miracle happens"). For Penetratin and R9/TAT, the authors consider that water pore and inverted micelle formation are incompatible. This is a bit rapid as inverted micelles might induce water pores through W/lipids interactions requiring less R residues and, possibly, less energy. This provides the opportunity to signal that, in spite of their very high number, key references are missing or hidden in cited reviews, some of them written by colleagues who are not among the main contributors to the CPP field.

Page 7 {section sign} 1 Fig. 1b confirms that Raji cells provide a good model for loss and gain of function (lovely rescue experiment) and that the authors should drop the two other cell types that provide no decisive information.

Page 8 {section sign} 1 Supp. Fig. 6b (no serum conditions) allows for the use of "normal" CPP concentrations and suggests that a fraction of the peptides may bind to serum components. No arrows in Supp. Fig.6b (but in 6c), and the R/pyrene butyrate interaction is not in 6c but in 6a. Still for Supp. Fig. 6c, the death of cells at 20µM (or less) even in the absence of K+ channels, confirms that we are borderline in term of peptide toxicity. There is a confusion between Supp. Fig. 6d and 6e and a legend problem (6e is not described). Cell death is assessed in % of PI-positive cells. Does this securely distinguish between death and holes allowing for PI entry without death? The CPP is incubated in the presence of Pyrene butyrate, making the KO cells less resistant. How does that demonstrate that the potassium channels are not involved in the killing if the peptide is already in? Unless the KO is done after internalization (but the cells should be already dead or dying?). This lacks clarity.

Page 9 {section sign} 1 The conclusion that the diffuse staining does not come from endosomal escape is based on the certainty that LLOME disrupts both endosomes and lysosomes. First, it should be verified with specific markers (rab5, rab7) that the fluorescent vesicles are endosomes. Second, the literature strongly suggests that LLOME primarily disrupts lysosomes and not endosomes. Finally, even if some endosomes are disrupted, the endosomal population is heterogenous and some CPPs may be in a subpopulation insensitive to LLOME. In addition, the importance of this issue is not well explained. In practice, access to the cytoplasm and nucleus requires crossing the plasma and/or the endosomal membrane and the latter, at least in early endosomes (thus the need of identifying the CPP-enriched vesicles), might not be very different from the plasma membrane. Page 9 {section sign} 2 Is Supp. Fig. 7e really necessary? First, as mentioned several times, if 20µM is a borderline concentration in term of toxicity, raising the concentration up to 100µM is problematic. Secondly, what matters is not "binding" in general, but binding to the proper membrane components. As mentioned by the authors themselves (Supp. Fig. 1e and movie), there are privileged sites of entry that may correspond to the recognition of specific molecular entities/structures.

Page 9 {section sign} 3 and Page 10 {section sign} 1 The authors should have used a construct that does not kill the cells much earlier, just after the screening experiments based on resistance to necrosis induced by TAT-rasGAP. For Supp. Fig 8a and b: I am fully convinced by Raji cells and HeLa cells but not by the SKW6.4 cells..

Page 10 {section sign} 2 Supp. Fig 9 is quite convincing but adds the information that 2µM are sufficient in neurons. This again makes the 20 to 80µM concentrations used on transformed cells unsatisfactory. If one needs a cell line (more user friendly than primary cultures), there are several neural ones that can be differentiated (SHY, LHUMES, etc.) that may have an appropriate membrane potential (below -90mV). Indeed, it would then be important to verify if pore formation is still induced by TAT, R9 and Penetratin (separately) on "naturally" hyperpolarized cells. Figure 2a confirms that changes in Vm are not solid for HeLa and SKW6.4 cells. This casts a doubt on the validity of the results obtained with the latter 2 cell lines.

Page 11 {section sign} 2 Why valinomycin was only tried on Raji cells?

Page 12 {section sign} 2 Looking at Fig. 2c, it seems that low Vm increases the uptake of all CPPs, except Transportan. Is there any reason why this Figure does not provide the number of vesicles per cell in the hyperpolarized conditions? In fact, if one goes to Supp. Fig. 9c, it appears that, among all peptides, only Penetratin is almost entirely cytoplasmic after 90' of incubation, whereas MAP and Transportan remain essentially vesicular. TAT and R9 are at mid-distance between these two extremes. This leads to send again the warning that all CPPs cannot be placed in a single category. The table that describes the sequences strongly suggests that, TAT and R9 uptake is due to the numerous Rs that cannot be replaced by Ks. In the case of Penetratin, that only has 3 Rs, the situation is thus different with the presence of 2 Ws previously shown to be mandatory for internalization, although absent in TAT ad R9. In Supp. Fig9, panel g is useless. A difference between peptides is also visible in Figure 2d where depolarization with KCl does not show the same efficiency on all peptides. The issue is whether these differences are significant and, if so, why? This discussion could be restricted to TAT, R9 and Penetratin. Supp. Fig. 10a also suggests that all peptides do not respond similarly to depolarization and that the effects differ between cell types and concentrations used. However, given the high concentrations used and the high variance between replicates, this figure might not be a priority in the reorganization of the manuscript.

Page 12 {section sign} 3 and Page 13 {section sign} 1 The pH story is either too long or too short.

Page 14 {section sign} 2 At low Vm values, there is a decrease in free energy barrier. Does this modify temperature-dependency for internalization? Do cells really require energy when the Vm is very low, like is often the case for neurons?

Page 15 {section sign} 2 Figure 2e is not explained, not even in the legend while the statement that CPPs induce a local hyperpolarization is central to the study.

Page 16 {section sign} 1 It is confusing that the same agent, here PI, is used to measure internalization (2 nm pore formation in response to hyperpolarization,) and cell death. I have seen the explanation below, but I do not find it fully satisfactory.

Page 16 {section sign} 2 Entry is not necessarily a size issue. Structure is an important parameter, including possible structure changes, for example in response to Vm modifications. Therefore, the statement that molecule with larger diameters are mostly prevented from internalization is not only vague ("mostly") but incorrect.

Page 17 {section sign} 4 and Page 18 {section sign} 1 In Supp. Fig. 13b and c, since the GAP domain is mutated, death is not due to RasGAP activity. So what causes zebrafish death (hyperpolarization?) The results seem contradictory with those of Supp. Fig 13f where survival is 100% at 48 h.

Page 18 {section sign} 2 The formation of inverted micelles is not incompatible with that of pores. CPP-induced hyperpolarization (Vm) is not measured directly, but deduced from experiments involving artificial membranes and in silico modeling. It would be useful to distinguish between what takes place on live cells (in vitro and in vivo) and what is speculated (based on modeling and artificial systems).

Page 19 {section sign} 3 The model posits that the number of Rs influences the ability of the CPPs to hyperpolarize the membrane and, consequently, to induce pore formation. Since pore formation is key to the addressing to the cytoplasm, how can one explain that Penetratin which has only 3 Rs is transported to the cytoplasm more readily that TAT or R9? The authors should take this contradiction in consideration and should not leave aside, in the literature, what does not fit with their model. The fact that that Rs cannot be replaced by Ks, both in R9 and Penetratin is explained by differences in deprotonization. This is interesting but speculative. It might be that the interaction between Rs versus Ks with lipids and sugars are different and not only based on charge. After all their atomic structures, beyond charges, are different.

Page 20 {section sign} 1 We still need to understand endosomal escape.

Major comments

• The key conclusions are convincing for a subset of CPPs and cell types
• Yes, some claims should be qualified as speculative, but not preliminary
• Many experiments should be removed. Neuronal primary cultures should be introduced to verify the main conclusions, at least for the 3 mains CPPs (TAT, R9, Penetratin). Answers must be given to the concentration issue. Vesicles should be characterized as well as the localization of the peptides in or around the vesicles. See above for less decisive but still important experiments that would benefit to the study.
• Yes, the requested experiments correspond to a reasonable costs and amount of time (10 to 20,000 € and 3 to 5 months of work)
• Yes, the methods are presented with great details. -Yes, the experiments are adequately replicated and statistical analysis is adequate

Minor comments (not so minor for some of them)

• See "Detailed analysis"
• No, prior studies are not referenced appropriately (see above)
• No, the text and figures are not clear and not accurate (see above)
• (i) use Raji cells and primary neuronal cultures, plus in vivo model and forget the other cell types; (ii) forget MAP and Transportan and compare TAT/R9 and Penetratin; (iii) drastically reduce the number of figures, tables and movies (6 primary figures, 6 supplemental figures and 4 tables are reasonable numbers; movies are not absolutely necessary); (iv) limit to 6 (max) the number of panels per figure; (v) limit the number of references to less than 50 and cite the primary reports rather than reviews); (vi) reduce the size of the Material and Methods and the length of figure legends.

Significance

• The mode of CPP internalization is an unanswered question and the report, if revised, will represent a conceptual and technical advance.
  • Bits and pieces of the conclusions can be found in previous reports. But the Vm-dependent pore formation as well as the CPP-induced "megapolarization" (even if only shown for a subset of CPPs) would be an important contribution. The authors must resist the tentation to generalize to all CPPs what might only be true for a few of them.
  • I do not have the expertise for the in-silico work, but my field of expertise allows me to understand all other aspects of the manuscript.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)): **Summary:** Previously, the authors showed the importance of contractile force in cell positioning and cell fate specification in preimplantation mouse development. In this study, the authors generated maternal-zygotic mutants of the non-muscle myosin-II heavy chain (NMHC) genes Myh9 and Myh10, and quantitatively analyzed their development using time-lapse microscopy and immunostaining. The authors first examined the expression of NMHCs. Myh9 and Mhy10 are present in preimplantation embryos, and Myh9 is maternally inherited. Single maternal-zygotic mutants of Myh9 or Myh10 revealed that maternal Myh9 plays a major role in actomyosin contractility. In maternal Myh9 mutants, compaction and contractility at the 8-cell stage were reduced. Maternal Myh9 mutants demonstrated a longer 8-cell stage, and mutant blastocysts had reduced cell numbers. Cell positioning was not affected; however, cell differentiation was slightly affected by reduced expression of TE and ICM markers. Maternal Myh9 mutants formed blastocoels, but lumen opening was observed earlier than that in wild-type embryos. In double maternal-zygotic mutants of Myh9 and Myh10, cytokinesis was severely affected. Nevertheless, TE fate was specified and embryos formed blastocoels. Interestingly, single-celled mutants swelled upon the formation of fluid-filled vacuoles in their cytoplasm. Similar TE fate specifications and cytoplasmic vacuoles were also observed with single-celled embryos produced by blastomere fusion. Based on these results, the authors concluded that maternal Myh9 is the major NMHC. However, Myh10 can significantly compensate for the loss of Myh9, and that cell fate specification and morphogenesis are independent of the success of cell division. **Minor comments:** Overall, the conclusions of this study are supported by high-quality data. However, I have a few minor concerns:

We thank the referee for her/his careful analysis of our manuscript.

1. Line 200~205. The authors showed the correlation between the cell number at the blastocyst stage and the 8-cell stage, and concluded that "the lengthened 8-cell stage of mzMyh9 is an important determinant of their reduced cell number at the blastocyst stage". This conclusion is not well supported because of several reasons. First, the timing of cell count is not clear. Cell number was compared at the blastocyst stage, but Figure 1c shows that mzMyh9 embryos initiate blastocoel formation earlier than wild-type embryos. Therefore, if cell count timing was determined based on the blastocyst morphology of the embryos, the timing of cell count (i.e., time after 3rd cleavage) for mzMyh9 mutants is earlier than that observed for wild-type embryos. This shorter culture time likely contributes to the reduced cell number of mzMyh9. Second, the authors only showed a correlation, and no experimental data supporting this conclusion were shown. If the cell number was counted at the same time after the 3rd cleavage, and if the authors' hypothesis is correct, then culturing mzMyh9 mutants for an additional three hour, which is the difference in the duration of the 8-cell stage, should make the cell numbers of mutants comparable to those of wild-type blastocysts.

Although, this correlation provides the best explanation we had based on the data, we agree that the statement above is weakly supported by our study. We do not want to make a strong point about it since we do not think it brings much to the narrative of the study. We have removed the sentence.

Discussion. In the paragraph starting from line 405, the authors discussed the inconsistencies in the observation of the phenotypes of mzMyh9 and mzMyh10 mutants with the conclusions of previous studies by others about cell polarization. It will be informative to also discuss about inconsistency with their previous observations on cell fate. In their previous report (reference 8), the authors concluded that without contractile forces, blastomeres adopt an inner-cell-like fate regardless of their position. This is clearly opposite of the phenotype of mzMyh9;mzMyh10 mutants, in which all the cells are specified to TE. Please add a discussion addressing this discrepancy.

The data provided here are consistent with the ones from ref 8 (Maître et al, 2016): reduced contractility (Myh9 KO, double Myh9;Myh10 KO or Blebbistatin treatment) leads to reduced CDX2 levels. In ref 8, CDX2 and YAP are checked at the 16-cell stage, before the definitive differentiation into TE and ICM, whereas here we present data at the mid-blastocyst stage (~64 cells). We had not checked SOX2 in ref 8 since it is not expressed at such early stage, so we cannot conclude about this marker.

We want to clarify that, as stated in the manuscript, in mzMyh9;mzMyh10 KO we detect CDX2 in 5/7 embryos only and therefore not all cells are correctly specified into TE. However, SOX2 could be detected in the inner cell of the one embryo that produced an inner cell. We had not discussed this issue further since it is difficult to conclude much from such rare events and we would prefer to keep it as such.

To strengthen our argument about reduced differentiation in NMHC mutant embryos, we now provide YAP immunostaining (Fig S4). YAP is correctly patterned in Myh10 mutants and shows slightly less defined nuclear localization in Myh9 mutants, in agreement with our previous observations on CDX2 in the present study and previous observations on YAP at the 16-cell stage (Maître et al 2016).

Together, we can conclude that, at the 16-cell stage, when ICM fate is not engaged yet (no detectable SOX2 expression), “inhibition of contractility causes (…) blastomeres to become inner-cell-like with respect to (…) Yap localization and Cdx2 levels, despite their external position” (Maître et al, 2016). At the blastocyst stage embryos with chronically impaired contractility can succeed in some but not all cases to produce TE (this study). Between these two developmental stages, blastomeres are exposed to prolonged signals from the apical domain and can be strongly deformed by the growing lumen. Based on the literature (Hirate et al 2013, Dupont et al 2011), both of these stimuli could potentially favor YAP nuclear localisation despite low contractility.

Throughout the paper, the description of gene and protein symbols should follow the rules of MGI's guidelines for nomenclature of genes (http://www.informatics.jax.org/mgihome/nomen/gene.shtml#gene_sym). Gene and allele symbols are italicized. Protein symbols use all uppercase letters and are not italicized.

We have corrected this.

Line 163. The term "contact angles" are used without any explanation or definition. The term should be introduced with a brief explanation in the text, preferably with a figure. It should help facilitate the understanding of the scientists working in different fields.

We have labelled a contact angle on Fig 1A and specified this in the text and in the figure legend.

Reviewer #1 (Significance (Required)): The importance of actomyosin contractility in compaction, cell polarization, cell positioning, and cell fate specification in preimplantation embryos has been reported by several groups, mostly using chemical inhibitors, except for the study cited in reference 8, in which chimeras of wild-type and mMyh9 mutant embryos were used. This is the first genetic analysis of the roles of actomyosin contractility in the development of preimplantation embryos. Thus, the major advancement of this study is the genetic dissection of the roles of actomyosin contractility in preimplantation mouse development, and clarifying the contribution of maternal/zygotic Myh9 and Myh10 genes. While the phenotypes of reduced compaction and blastomere contractility are consistent with those observed in previous studies, polarization and TE fate specification of the mutant cells appear inconsistent with the conclusions of previous inhibitor experiments, which show defects in polarization processes and fate specification to ICM. These are potentially important issues, but detailed analyses were not performed. The requirement of actomyosin contractility for the cytokinesis of preimplantation embryos is also a novel finding, although it is expected from studies conducted in other systems. Vacuole formation in single-celled mzMyh9;mzMyh10 mutants in a timely manner suggested that fluid accumulation is a cell autonomous process and that cell differentiation occurs independently of cell division. These are also novel findings, although the latter is somewhat expected from previous studies performed using cell number manipulated embryos. In summary, the conceptual advance offered by this study is small. However, this is a high-quality study and makes critical observations in the field of preimplantation mouse development. Scientists in the field of developmental biology, especially those working on preimplantation development, should be interested in this paper. My field of expertise is preimplantation development.

We thank the reviewer for her/his appreciation of our work. We want to argue that we did perform a very detailed analysis of the development of the NMHC mutant embryos, with multiple quantitative image and data analyses to thoroughly and objectively characterise the phenotypes of these mutants. If by “detailed analysis”, the reviewer meant a molecular dissection of the phenotype, we argue that 1/ checking the end result (i.e. presence of TE and ICM markers, presence of polarised fluid transport) was sufficient to assess the functionality of biological processes without checking every steps of a signalling cascade; 2/ we now provide additional molecular information on the state of YAP and apico-basal polarisation (Fig S3-4).

Reviewer #2 (Evidence, reproducibility and clarity (Required)): In this manuscript, Schliffka et al. report that maternally deposited Myh9 is the major NMHC in preimplantation embryonic morphogenesis and complete removal of both Myh9 and Myh10 caused severe cytokinesis failure similar to tissue culture cells. Interestingly, although the mutant embryos completely failed cytokinesis thus forming single-celled embryos, they initiated trophoblast gene expression and vacuolization (likely similar to blastocoel formation), suggesting that the timing of preimplantation developmental events is independent from cell number and morphogenetic events.

We thank the reviewer for her/his appreciation of our work.

Major comments Vacuolization in single-celled embryos is interesting. In the images, there looks to be two types of vacuoles, F-actin positive and negative. The authors speculate the similarity to blastocoel formation. To support this, it is important to stain them with some basolateral markers like Na+ ATPase, E-cadherin and B-catenin. It is also important to confirm if the apical domain is properly formed by staining the apical domain markers like aPKC and Pard6.

We thank the reviewer for this suggestion. We now provide immunostaining of single Myh9 or Myh10 and double Myh9;Myh10 mutants for aPKC (PRKCz), Na/K ATPase (ATP1A1), Aquaporin-3 (AQP3), the best basolateral marker in our hands, which is also very relevant to fluid pumping, CDH1 and F-actin (Fig S3). We observe that these markers localise similarly in multiple-celled and single-celled embryos, suggesting that vacuoles de facto substitute for the basolateral compartment normally consisting of cell-cell contacts and the lumen. This suggests that the same machinery is at the origin of the fluid inside the lumen and inside vacuoles.

Minor comments All gene names should be Italicized.

We have corrected this.

L157. Myh10 and Myh9 should be mMyh10 and mMyh9.

We have corrected this.

L294 1/8 embryos. What does this mean?

This means this was observed in 1 embryo out of 8 in total.

L333 6/25 embryos. Does this mean 6 out of 25 embryos combined all maternal double mutants?

Precisely.

L438-442. I do not find these embryos are similar to tetraploid embryos. I suggest to remove the sentences.

We have removed the sentences.

Reviewer #3 (Evidence, reproducibility and clarity (Required)): This study investigates the roles of non-muscle myosin in development, reporting a requirement for maternal and zygotic Mhy9 and 10. Strengths of the study include robust genetic techniques, innovative nested imaging to visualize events over different timescales within the same embryos, and analysis of morphological as well as transcriptional/cell fate phenotypes. However, the somewhat superficial phenotype analysis limits the authors' ability to draw strong mechanistic conclusions about what is going on in these mutants. Is cell polarization normal? Is cell signaling (HIPPO signalling) normal?

We thank the reviewer for carefully assessing our study. We argue that we have thoroughly characterized the phenotypes of the NMHC mutants, which allowed us to draw many important mechanistic conclusions (such as the ability of NMHC mutants to polarise, or to pump fluid in a cell autonomous manner). Each mutant embryo has been imaged at multiple time scales, stained and genotyped. The time-lapses and immunostaining have been extensively quantified using manual as well as automated methods such as particle image velocimetry. We also provided fusion experiments, which phenocopy some aspects of the mutants to provide evidence of the mechanisms causing the observed phenotype.

Nevertheless, we agree that one can always do more and that we had focused on the biological processes (lineage specification, morphogenesis and cleavages) rather than molecular characterisation. Although polarised fluid pumping ascertains a functioning epithelial polarity, we now provide immunostaining of polarity markers in mutant embryos. Although CDX2 and SOX2 staining inform on the output of the signalling cascade leading to effective TE and ICM differentiation, we now provide YAP immunostaining of mutant embryos. We hope this satisfies the request from the reviewer.

What determines whether an embryo can form an inside cell or not?

This is an outstanding question. Cells can internalise by oriented cell division or contractility mediated cell sorting. Contractility-mediated internalisation functions with only 2 cells (as when doublets of 16-cell stage blastomeres form a cell-in-a-cell structure) but requires to grow above a tension asymmetry threshold (of 1.5 in WT and most likely above 3 in these mutants due to their poor compaction, see Maître et al 2016). Oriented cell division only works if there is a cell-cell contact to push dividing cells in between. Therefore, at least 3 cells are required for an inner cell to be internalised by this mechanism.

In double mutants, the average cell number is 2.9. No embryo consisting of only 2 cells contained an inner cell, about half of embryos with 3-5 cells contained a single inner cell and all embryos with 6 cells or more contained inner cells (Fig 4D). Based on the low contractility of double mutants, we can speculate that they do not succeed in overcoming the tension asymmetry threshold. This would explain why no inner cell is observed in embryos with only 2 cells. We can speculate that with 3-5 cells, oriented divisions could occur thanks to the presence of functional polarity (Korotkevitch et al 2017).

We have added a discussion about this important matter.

Similarly, the manuscript would benefit from rewriting to reframe the authors' discoveries within the context of what is known regarding lineage specification (e.g., why does CDX2/SOX2 expression indicate normal lineage specification). Additional minor comments are listed below.

We elaborate on these points.

**Minor comments:** • Introduction focuses overly on the work of the PI and his mentor, giving the presentation an unnecessarily biased quality.

We have corrected this to the best of our ability. Please note that, to our knowledge, there are 8 studies (Anani et al., 2014; Maître et al., 2015; Samarage et al., 2015; Maître et al., 2016; Zhu et al., 2017; Zenker et al., 2018; Chan et al., 2019; Dumortier et al., 2019) looking in more or less details into the contractility of the preimplantation embryo. We mention and cite all of these studies.

• The text asserts that Myh9 levels are highest during zygote stage, on the basis of qPCR (Fig. S1A), and that this is also observed by RNA-seq (Fig. S1B). However, this conclusion is not supported by the data shown.

We have corrected this.

• Would be nice to repeat the qPCR on the mz null.

We agree with the referee that this would help in assessing the level of compensation between NMHC paralogs in individual mutants. Our qPCR protocol requires a few tens of embryos to be able to amplify the different paralogs. Unfortunately, pooling embryos from our current mating strategy would result in pooling homozygote and heterozygote mutants as we cannot know a priori which embryo is of which genotype.

We believe that, as nice as this information would be, the current study does not require this information, which would be technically challenging.

• Were the measurements shown in Fig. S1F taken from the images shown in Fig. S1E? If so, the authors should clarify how the measurements were normalized, since the images in Fig. S1E were clearly taken with different camera settings (as judged by background fluorescence level surrounding the embryos).

The camera settings were identical but the LUT are set differently (to the maximal signal of a given genotype) so that some signal is visible. The signal intensities are so different between genotypes that if set to a common LUT, we either get the maternal GFP as a saturated white circle or the other genotypes as black images. We explain our LUT settings both in the methods and figure legends.

As an alternative to the current data presentation, we would be fine to have the same LUT for all images and show almost black images for WT and paternal GFP.

• Can't really conclude that Myh9 is essential for compaction since compaction occurs (albeit abnormally) in the absence of Myh9 (line 177-178).

Our statement is “we conclude that maternal Myh9 is essential for embryos to compact fully”. WT and mzMyh10 mutants increase their contact angles by 60° whereas mzMyh9 only grow by 30°. Double mutants compact less than single Myh9 mutants. Therefore, the compaction movement is halved in mzMyh9 and the residual weak compaction could be explained by compensation from Myh10. We stand by our statement.

• Line 211: "observe" rather than "measure".

We have corrected this.

• If the embryos achieve proper ICM/TE ratio, in spite of having half the number of cells in the mutants, is that to be expected? Would/do halved embryos also possess the same ICM/TE ratio? Or is this outcome peculiar to the mutants?

This is an interesting question on which we had not sufficiently elaborated. Our experiments with cell fusion at the 4-cell-stage (Fig. S5) produced embryos with reduced cell number. These resemble Myh9 mutant embryos in the aspect that they show a reduced cell number while maintaining the total embryonic cell mass. In both cases, the ICM/total cell ratio is similar to control embryos. This indicates a robust mechanism of ICM/TE ratio setting that is robust to the cell number change observed in the single mutant. We have added a discussion about this.

• Line 222: what is the evidence that Cdx2 and Sox2 are TE and ICM markers?

We have added references to the studies from Strumpf et al., 2005 and Avilion et al., 2003 to support these claims.

• Is the reported reduction in CDX2 and SOX2 levels due to a stage-delay? What would the comparison look like in wt embryos with half as many cells? Timing of lumen formation may or may not indicate developmental timing...

We address this point by fusing embryos to half the cell number and find that the fate marker levels are specifically affected as a result of mutation of Myh9 (Fig S5).

We agree that the timing of lumen formation is unlikely to be a good reference for staging and we did not use this event. We do synchronise embryos based on lumen opening only when comparing lumen growth rate.

• Line 240 - what was the correction on the multiple pairwise comparisons (multiple t tests)?

To compare lumen growth rate, individual growth rates of mutants are compared to those of WT using Student’s t test. Growth rates are considered as normally distributed and independent (not pairwise).

• Lumen forms on time in mutants, despite having fewer cells. Alternatively, lumen forms early, prior to acquisition of proper cell number. Is there a reason the authors did not consider this alternative?

The referee is correct. Lumens form with fewer cells in mutant embryos and therefore prior to the acquisition of proper cell number.

• Lines 306 and 339: why does lack of SOX2 expression suggest that the lineage specification program is intact? Why does expression of CDX2 suggest TE initiation has occurred normally? The regulation of these two markers was not introduced.

We have better introduced and justified this aspect.

• Line 349: why is blastocoel formation a cell-autonomous property when it clearly occurs extracellularly? Does this also happen in wild type embryos?

Blastocoel formation is clearly a multi-cellular process. We argue that fluid accumulation is not. The implications for WT embryos are that fluid can be accumulated in the blastocoel entirely trans-cellularly (no need for fluid to flow through cell-cell junction).

• Speculate in Discussion on why the ML-7/Blebbistatin experiments results could differ from the genetic results produced here.

Blebbistatin experiments are in agreement with the mutant data. ML-7 experiments are partially in agreement with the mutant data. The discrepancy lies in the effect on cell polarity. ML-7 affects kinases other than the MLCK, such as PKC, which is a known regulator of cell polarity during preimplantation development. Although this is speculative, we specify this in the revised manuscript.

• Can these mutant embryos implant?

We grow colonies of heterozygous mutants, therefore mMyh9, mMyh10 and mMyh9;mMyh10 embryos are viable and must be able to implant. As for homozygous mutants, they are not viable and we do not know whether they can implant.

Reviewer #3 (Significance (Required)): The study provides the first strong evidence of a requirement for non-muscle myosin in epithelialization. This is significant to embryology and to epithelial biology.

We thank the reviewer for appreciating the significance of our study. We want to clarify that our study provides evidence for NMHC as NOT being required for de novo epithelialization.

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Referee #3

Evidence, reproducibility and clarity

This study investigates the roles of non-muscle myosin in development, reporting a requirement for maternal and zygotic Mhy9 and 10. Strengths of the study include robust genetic techniques, innovative nested imaging to visualize events over different timescales within the same embryos, and analysis of morphological as well as transcriptional/cell fate phenotypes. However, the somewhat superficial phenotype analysis limits the authors' ability to draw strong mechanistic conclusions about what is going on in these mutants. Is cell polarization normal? Is cell signaling (HIPPO signalling) normal? What determines whether an embryo can form an inside cell or not? Similarly, the manuscript would benefit from rewriting to reframe the authors' discoveries within the context of what is known regarding lineage specification (e.g., why does CDX2/SOX2 expression indicate normal lineage specification). Additional minor comments are listed below.

Minor comments:

• Introduction focuses overly on the work of the PI and his mentor, giving the presentation an unnecessarily biased quality.

• The text asserts that Myh9 levels are highest during zygote stage, on the basis of qPCR (Fig. S1A), and that this is also observed by RNA-seq (Fig. S1B). However, this conclusion is not supported by the data shown.

• Would be nice to repeat the qPCR on the mz null.

• Were the measurements shown in Fig. S1F taken from the images shown in Fig. S1E? If so, the authors should clarify how the measurements were normalized, since the images in Fig. S1E were clearly taken with different camera settings (as judged by background fluorescence level surrounding the embryos).

• Can't really conclude that Myh9 is essential for compaction since compaction occurs (albeit abnormally) in the absence of Myh9 (line 177-178).

• Line 211: "observe" rather than "measure".

• If the embryos achieve proper ICM/TE ratio, in spite of having half the number of cells in the mutants, is that to be expected? Would/do halved embryos also possess the same ICM/TE ratio? Or is this outcome peculiar to the mutants?

• Line 222: what is the evidence that Cdx2 and Sox2 are TE and ICM markers?

• Is the reported reduction in CDX2 and SOX2 levels due to a stage-delay? What would the comparison look like in wt embryos with half as many cells? Timing of lumen formation may or may not indicate developmental timing...

• Line 240 - what was the correction on the multiple pairwise comparisons (multiple t tests)?

• Lumen forms on time in mutants, despite having fewer cells. Alternatively, lumen forms early, prior to acquisition of proper cell number. Is there a reason the authors did not consider this alternative?

• Lines 306 and 339: why does lack of SOX2 expression suggest that the lineage specification program is intact? Why does expression of CDX2 suggest TE initiation has occurred normally? The regulation of these two markers was not introduced.

• Line 349: why is blastocoel formation a cell-autonomous property when it clearly occurs extracellularly? Does this also happen in wild type embryos?

• Speculate in Discussion on why the ML-7/Blebbistatin experiments results could differ from the genetic results produced here.

• Can these mutant embryos implant?

Significance

The study provides the first strong evidence of a requirement for non-muscle myosin in epithelialization. This is significant to embryology and to epithelial biology.

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, Schliffka et al. report that maternally deposited Myh9 is the major NMHC in preimplantation embryonic morphogenesis and complete removal of both Myh9 and Myh10 caused severe cytokinesis failure similar to tissue culture cells. Interestingly, although the mutant embryos completely failed cytokinesis thus forming single-celled embryos, they initiated trophoblast gene expression and vacuolization (likely similar to blastocoel formation), suggesting that the timing of preimplantation developmental events is independent from cell number and morphogenetic events.

Major comments

Vacuolization in single-celled embryos is interesting. In the images, there looks to be two types of vacuoles, F-actin positive and negative. The authors speculate the similarity to blastocoel formation. To support this, it is important to stain them with some basolateral markers like Na+ ATPase, E-cadherin and B-catenin. It is also important to confirm if the apical domain is properly formed by staining the apical domain markers like aPKC and Pard6.

Minor comments

All gene names should be Italicized.

L157. Myh10 and Myh9 should be mMyh10 and mMyh9.<br> L294 1/8 embryos. What does this mean?

L333 6/25 embryos. Does this mean 6 out of 25 embryos combined all maternal double mutants?

L438-442. I do not find these embryos are similar to tetraploid embryos. I suggest to remove the sentences.

Significance

In this manuscript, Schliffka et al. report that maternally deposited Myh9 is the major NMHC in preimplantation embryonic morphogenesis and complete removal of both Myh9 and Myh10 caused severe cytokinesis failure similar to tissue culture cells. Interestingly, although the mutant embryos completely failed cytokinesis thus forming single-celled embryos, they initiated trophoblast gene expression and vacuolization (likely similar to blastocoel formation), suggesting that the timing of preimplantation developmental events is independent from cell number and morphogenetic events.

Major comments

Vacuolization in single-celled embryos is interesting. In the images, there looks to be two types of vacuoles, F-actin positive and negative. The authors speculate the similarity to blastocoel formation. To support this, it is important to stain them with some basolateral markers like Na+ ATPase, E-cadherin and B-catenin. It is also important to confirm if the apical domain is properly formed by staining the apical domain markers like aPKC and Pard6.

Minor comments

All gene names should be Italicized.

L157. Myh10 and Myh9 should be mMyh10 and mMyh9.<br> L294 1/8 embryos. What does this mean?

L333 6/25 embryos. Does this mean 6 out of 25 embryos combined all maternal double mutants?

L438-442. I do not find these embryos are similar to tetraploid embryos. I suggest to remove the sentences.

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Referee #1

Evidence, reproducibility and clarity

Summary:

Previously, the authors showed the importance of contractile force in cell positioning and cell fate specification in preimplantation mouse development. In this study, the authors generated maternal-zygotic mutants of the non-muscle myosin-II heavy chain (NMHC) genes Myh9 and Myh10, and quantitatively analyzed their development using time-lapse microscopy and immunostaining. The authors first examined the expression of NMHCs. Myh9 and Mhy10 are present in preimplantation embryos, and Myh9 is maternally inherited. Single maternal-zygotic mutants of Myh9 or Myh10 revealed that maternal Myh9 plays a major role in actomyosin contractility. In maternal Myh9 mutants, compaction and contractility at the 8-cell stage were reduced. Maternal Myh9 mutants demonstrated a longer 8-cell stage, and mutant blastocysts had reduced cell numbers. Cell positioning was not affected; however, cell differentiation was slightly affected by reduced expression of TE and ICM markers. Maternal Myh9 mutants formed blastocoels, but lumen opening was observed earlier than that in wild-type embryos. In double maternal-zygotic mutants of Myh9 and Myh10, cytokinesis was severely affected. Nevertheless, TE fate was specified and embryos formed blastocoels. Interestingly, single-celled mutants swelled upon the formation of fluid-filled vacuoles in their cytoplasm. Similar TE fate specifications and cytoplasmic vacuoles were also observed with single-celled embryos produced by blastomere fusion. Based on these results, the authors concluded that maternal Myh9 is the major NMHC. However, Myh10 can significantly compensate for the loss of Myh9, and that cell fate specification and morphogenesis are independent of the success of cell division.

Minor comments:

Overall, the conclusions of this study are supported by high-quality data. However, I have a few minor concerns:

1. Line 200~205. The authors showed the correlation between the cell number at the blastocyst stage and the 8-cell stage, and concluded that "the lengthened 8-cell stage of mzMyh9 is an important determinant of their reduced cell number at the blastocyst stage". This conclusion is not well supported because of several reasons. First, the timing of cell count is not clear. Cell number was compared at the blastocyst stage, but Figure 1c shows that mzMyh9 embryos initiate blastocoel formation earlier than wild-type embryos. Therefore, if cell count timing was determined based on the blastocyst morphology of the embryos, the timing of cell count (i.e., time after 3rd cleavage) for mzMyh9 mutants is earlier than that observed for wild-type embryos. This shorter culture time likely contributes to the reduced cell number of mzMyh9. Second, the authors only showed a correlation, and no experimental data supporting this conclusion were shown. If the cell number was counted at the same time after the 3rd cleavage, and if the authors' hypothesis is correct, then culturing mzMyh9 mutants for an additional three hour, which is the difference in the duration of the 8-cell stage, should make the cell numbers of mutants comparable to those of wild-type blastocysts.
2. Discussion. In the paragraph starting from line 405, the authors discussed the inconsistencies in the observation of the phenotypes of mzMyh9 and mzMyh10 mutants with the conclusions of previous studies by others about cell polarization. It will be informative to also discuss about inconsistency with their previous observations on cell fate. In their previous report (reference 8), the authors concluded that without contractile forces, blastomeres adopt an inner-cell-like fate regardless of their position. This is clearly opposite of the phenotype of mzMyh9;mzMyh10 mutants, in which all the cells are specified to TE. Please add a discussion addressing this discrepancy.
3. Throughout the paper, the description of gene and protein symbols should follow the rules of MGI's guidelines for nomenclature of genes (http://www.informatics.jax.org/mgihome/nomen/gene.shtml#gene_sym). Gene and allele symbols are italicized. Protein symbols use all uppercase letters and are not italicized.
4. Line 163. The term "contact angles" are used without any explanation or definition. The term should be introduced with a brief explanation in the text, preferably with a figure. It should help facilitate the understanding of the scientists working in different fields.

Significance

The importance of actomyosin contractility in compaction, cell polarization, cell positioning, and cell fate specification in preimplantation embryos has been reported by several groups, mostly using chemical inhibitors, except for the study cited in reference 8, in which chimeras of wild-type and mMyh9 mutant embryos were used. This is the first genetic analysis of the roles of actomyosin contractility in the development of preimplantation embryos. Thus, the major advancement of this study is the genetic dissection of the roles of actomyosin contractility in preimplantation mouse development, and clarifying the contribution of maternal/zygotic Myh9 and Myh10 genes. While the phenotypes of reduced compaction and blastomere contractility are consistent with those observed in previous studies, polarization and TE fate specification of the mutant cells appear inconsistent with the conclusions of previous inhibitor experiments, which show defects in polarization processes and fate specification to ICM. These are potentially important issues, but detailed analyses were not performed. The requirement of actomyosin contractility for the cytokinesis of preimplantation embryos is also a novel finding, although it is expected from studies conducted in other systems. Vacuole formation in single-celled mzMyh9;mzMyh10 mutants in a timely manner suggested that fluid accumulation is a cell autonomous process and that cell differentiation occurs independently of cell division. These are also novel findings, although the latter is somewhat expected from previous studies performed using cell number manipulated embryos. In summary, the conceptual advance offered by this study is small. However, this is a high-quality study and makes critical observations in the field of preimplantation mouse development. Scientists in the field of developmental biology, especially those working on preimplantation development, should be interested in this paper. My field of expertise is preimplantation development.

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Reply to the reviewers

We thank Review Commons and its three reviewers for your supportive and insightful responses to our manuscript. Below, we provide detailed responses to the reviewers’ individual comments and how we plan to address them during the revision.

Reviewer #1: **Major comments:**

The manuscript is very well written. The data is clearly presented. The methods are explained in sufficient detail with a few exceptions mentioned below, and statistical analysis are adequate. There are some concerns and suggestions about the experimental design and data presentation.

- Drug treatments. It is not clear whether the cells were previously grown on charcoal-stripped serum before hormone treatments. From methods, it seems they were grown in 5% FBS and directly treated with the hormones. Also, what "hormone-free medium" mean? Is it charcoal stripped Serum or not Serum at all?

For all experiments, the cells were grown in medium containing 5% FBS. Throughout the manuscript, “hormone-free” refers to medium containing 5% FBS with no dexamethasone added. Technically, this medium is not hormone-free as FBS contains low levels of cortisol. However, the levels of cortisol from the FBS in our medium seems insufficient to elicit a transcriptional response or DNA binding by GR based on experiments comparing charcoal stripped and medium containing regular 5% FBS. However, we acknowledge that it should be made clear to the reader that growth conditions technically were not hormone-free. We will make sure to include this information in both the methods and results section of a revised manuscript. In addition, we will state explicitly that our naiive cells are those that have not been exposed to a high dose of hormone.

Replicates for these data sets? The ATAC and Chip-Seq should have at least 2. The concordance of the ATAC-seq and Chip-seq replicates should be described and shown in supplemental figures.

The ChIP-seq peaks for GR are the intersect of two biological replicates. This is described in the Methods section (page 7). For the ATAC data, we used two biological replicates for the vehicle treated cells and treated two different hormones (dexamethasone and cortisol) as replicates. In a revised manuscript, we will add a supplemental figure to show the concordance between the replicates.

Fig1A - The ATAC-seq HM should be clustered to show which peaks in opening/closing and unchanged peaks also have called GR chip peaks. Showing browser shots as in Fig1B is cherry picking data and can be put in a supplementary figure as an example. This is a main point of emphasis of the manuscript so show the data. The atac peaks that do overlap with GR chip peaks should be sorted by GR peak intensity. The QPCR is then only needed to confirm the quantitative changes.

This is a good idea. As suggested by this reviewer (and also in response to a comment by one of the other reviewers), we will revise this figure panel to make the overlap between GR binding and opening and closing sites more obvious. Here are the numbers:

A549 cells:

opening sites: 49%

closing: 10%

nonchanging: 18%

U2OS cells:

opening: 54%

closing: 0.2%

nonchanging: 7%

Regarding the use of browser shots, obviously these are cherry picked examples, however in our opinion they serve a purpose beyond illustrating examples of individual loci that open or close as they also give the reader an idea of the quality of the ATAC-seq data.

To show both the ATAC sites and H3K27ac sites are specific to hormone treatment, a random set of 15K peaks not in this peak set also should be shown in HMs and should not change with the treatments. Why does the H3K27ac go down in the 6768 non changing sites with dex?

The proposed group of control peaks is essentially what we included as “non-changing” peaks. For the revision, we will refine this group and compare the H3K27ac signal between GR-occupied and non-occupied groups. Regarding reduced H3K27ac signal upon Dex treatment at non-changing sites: Notably, this comparison is based on a single ChIP-seq replicate. In our experience, ChIP-seq experiments show quite some variability between biological replicates, which limits our ability to compare signal levels quantitatively. Thus, the difference could simply reflect a difference in ChIP efficiency between the treated and untreated cells. Alternatively, it could be that there is a general redistribution of H3K27ac signal towards GR-occupied opening sites. To pin down which of these explanations is valid, we would need to perform additional experiments, e.g. using spike-ins. However, this is beyond what we can do at the moment and therefore, we will instead revise the text to make sure that the interpretation of these results is somewhat speculative.

The D & E parts of Fig1 can then be eliminated to become parts of Fig1A. Its not clear in the text that the HMs in Fig1 are all sorted in the same way.

We will revise figure 1 as requested. In our initial submission, the data was always sorted by signal intensity of the feature shown. We will revise this and sort by ATAC-signal and keep a consistent sorting order for other features shown (and stratify each group into GR-occupied or not).

- Fig. 1b (and d). The ChIP data is from 3h-hormone treatment while the ATAC-seq data is from a 20h hormone treatment. It seems a bit misleading to directly compare GR occupancy with the state of the chromatin at different time windows. Shouldn't the authors show their ATAC-seq 4h treatment data (shown in Fig S1) here instead?

We will revise the figures as suggested to show the same time point for ChIP and ATAC-seq data.

- Fig. 1f. The authors state "downregulated genes only show a modest enrichment of GR peaks". However, there is a significant enrichment of GR-peaks in repressive genes compared to non-regulated genes. It would be interesting to see how some of these peaks look in a browser shot. While the general conclusion "transcriptional repression, in general, does not require nearby GR binding", seems valid, the observation that many GR peaks appear directly bound to nearby repressed genes ought to be more emphatically recognized in the text.

This is a fair point and was also raised by the other reviewers. During the revision, we will make textual changes to acknowledge that GR binding is enriched near repressed genes, albeit less so than for activated genes. In addition, we will include genome browser shots of genes with nearby peaks that are repressed by GR.

- Concept of naïve cells (Fig. 3A). If cells are normally grown in serum-containing media, which is known to have some level of steroids, can the cells described here as "Basal expression" be truly free of a primed state? In the first part of the experimental design (+/- 4h hormone), which type of media is present here? Is it 5% FBS? A concern is that the authors may require the assumption that the (4h + 24h) period a is sufficient to erase all memory of the cells, which is exactly what they are trying to test.

See our response to the first major comment above.

It would be interesting to do a time course of the hormone-free period of the washout to determine the memory of the chromatin environment that results in the enhanced transcriptional response instead of just 24 and 48 hrs in A549 cells.

We agree that that would be interesting but this is something that we cannot include for now.

Fig 5A appears to show H3K27ac overlaying H3K27me marks near the promoter of ZBTB16 and at the GR sites within the gene locus with no reduction in H3K27me levels. This seems counterintuitive and should be explained or addressed especially since the authors use quantitative comparisons of H3K27ac levels with and without treatment in other figures.

A trivial explanation for the overlaying H3K27ac and H3K27me3 marks at the ZBTB16 locus is that the ChIP results represent a population average. From our single-cell FISH experiments, we found that only a subset of cells activates ZBTB16 expression upon hormone treatment. Thus, a potential explanation is that the cells of the population that respond are responsible for the H3K27ac signal whereas the non-responders are decorated with H3K27me3. We will include this information in a revised discussion.

Showing the changes of ZBTB16 upon 2nd stimulation via FISH is not terribly surprising and is even the most expected reason for higher RNA levels. Why does it only occur at that gene is a better question and is touched on in the discussion. It is more likely that this gene has a very low level of pre-hormone transcription compared to FKBP5 (see Fig 3e and the FISH images). ZBTB16 is in the lower 3rd of basemean RNA levels of GR responsive genes according to the RNAseq data. Selection of 1 or 2 other genes with similar basemean levels of RNA (from the RNA-Seq data) would make the data more

When compared to FKBP5, ZBTB16 indeed has very low levels of pre-hormone expression. However, this is unlikely to explain the observed “memory” for ZBTB16 given that there are other genes with similarly low pre-hormone levels that do not show more robust responses upon repeated hormone exposure (see Fig. 3B,D). For the FISH experiments, we decided to include a non-primed gene (FKBP5 as control). We agree that adding additional control genes with comparable basemean levels would be informative. For example, this would tell us if a response of only a subset of cells in the population to hormone is specific to ZBTB16. Based on single cell studies by others (PMID: 32170217), most GR target genes show a response in only a subset of cells indicating that this is unlikely a unique feature of ZBTB16 explaining the priming observed. Rather than performing additional experiments, we will revise the discussion to acknowledge the difference in basemean and the potential role of cell-to-cell variability in explaining the observed “memory” for the ZBTB16 gene.

**Minor comments:**

- In the Intro (paragraph two), the authors explain the different mechanisms by which GR might repress genes. One alternative the authors appear to have missed is the possibility of direct binding to GREs while, for example, recruiting a selective corepressor such as GRIP1 (Syed et al., 2020). There are many recent critics to the notion that transrepression via tethering is responsible for GR repressive actions at all (Escoter-Torres et al., 2020; Hudson et al., 2018; Weikum et al., 2017).

We are aware of these studies and agree that they should be included when listing the possible mechanisms by which GR can repress genes. We will revise the text accordingly.

- When the authors introduce the concept of tethering to AP-1, they go way back to the first description of tethering. However, one of the references (Ref 20) actually goes against the tethering model as they did not detect protein-protein interactions between AP-1 and GR, and also, they conclude that repression requires the DNA-binding domain.

We will pick a more appropriate reference indicative of tethering as a mechanism by which GR might repress genes.

-Figure 2. The authors state "This suggests that the few sites with persistent opening are likely a simple consequence of an incomplete hormone washout and associated residual GR binding". The authors should check the subcellular distribution of GR after their washout protocol. If the washout is not completed, GR should still be in the nuclear compartment.

The careful phrasing here was to include the possibility that GR might bind DNA even when hormone is completely washed out. However, a more likely explanation is that the washout is incomplete. The residual GR binding we find in our ChIP assays shows us that a subset of GR is indeed still chromatin-bound which implies that some GR is still in the nuclear compartment.

- The first part of the manuscript (Repression through "squelching") seems a bit disconnected from the rest of the results (reversibility in accessibility). The abstract is structured in a way that this disconnection seems much less obvious. Perhaps the authors could try to present their squelching part in the middle of the manuscript, following the flow of the abstract? This is just a suggestion.

When revising the manuscript, we will see if implementiung this suggestion is feasible.

- Figures have CAPS panel letters (A,B,C, etc) while the text calls for lower case letter (a,b,c...)

We will fix this as part of the revision. Reviewer #2: **Major Comments**

We agree that long-term and repeated GC treatment would be very interesting to study and would yield insights that are more likely to be relevant to, for example, emerging GC-resistance during therapeutic use. We are aware of the limitations of our study and will make sure that these are acknowledged in the revised manuscript and we will point out the speculative nature of translating our findings to an in-vivo setting.

2a.) The authors show several heatmaps to indicate changes in accessibility, H3K27ac and P300 upon Dex treatment as well as GR binding patterns in Fig. 1 and S1. Those are sorted by decreasing signal strength (I assume). To make those results more comparable, I suggest to sort them all in the same way (e.g. by descending ATAC-Seq signal or fold-change).

A similar suggestion was made by reviewer 1. We agree that using the same sort order for the datasets makes it easier to link the different types of data we generated. We will present the data with a consistent sorting order and stratified by GR-occupied or not when we revise the manuscript.

2b.) In line with a.), it is unclear to the reader if those sides opening /closing are the same sides showing increased/decreased H3K27ac or P300 occupancy and if those sides bind GR. Integrating this data together with mRNA e.g as correlation plots would strengthen the author's argument that accessibility, H3K27ac and mRNA changes are indeed correlated. What about the GR binding sites that do not change accessibility or H3K27ac? What makes those different? ** Therefore, the statement "Furthermore, closing peaks, which show GC-induced loss of H3K27ac levels and lack GR occupancy (Fig. S1c-f), were enriched near repressed genes" on page 10 as well as the statement "suggesting that transcriptional repression by GR does not require nearby GR binding." in the abstract and discussion cannot be made from how the data is presented.

The first issue raised will be addressed by using the same sort order across different types of data. It might also shed light on features associated with GR binding sites that do not change accessibility or H3K27ac. Once we implement the revised sorting order, we will evaluate if the statements mentioned are indeed supported by the data.

2c.) Several recent studies have shown that GR's effect on gene expression and chromatin modification at enhancers might be locus-/context-specific ("tethering", competition, composite DNA binding) and/or recruitment of different co-regulators (see Sacta et al. 2018 (doi: 10.7554/eLife.34864), Gupte et al. 2013 (doi.org/10.1073/pnas.1309898110) and many more). Defining the GR-bound or opening/closing sides in terms of changing H3K27ac (or having H3K27ac or not) more closely would help to link those to gene expression changes e.g. in violin plots. Furthermore, the authors could include a motif analysis to see if the different enhancer behaviours can be explained by differences in the GR motif sequence or co-occurring motifs. Thereby more closely defining the mechanism of chromatin closure a sites that lack GR binding e.g. by displacement of other transcription factors as described for p65 in macrophages (Oh et al. 2017 (doi.org/10.1016/j.immuni.2017.07.012)). In general a more detailed analysis of the data is required before the authors could state "Instead, our data support a 'squelching model' whereby repression is driven by a redistribution of cofactors away from enhancers near repressed genes that become less accessible upon GC treatment yet lack GR occupancy." on page 10. The results might also be explained by competitive transcription factor binding, tethering or selective co-regulator recruitment (e.g. HDACs).

We will include a motif analysis comparing opening, closing and non-changing sites (stratified into GR-occupied or not) in a revised version of the manuscript. In addition, we will further investigate the redistribution of p300 upon Dex-treatment e.g. to test the correlation between p300 loss at closing sites lacking GR occupancy and transcriptional repression. We agree that the “squelching model” is just one of several explanations for repression and will provide a more comprehensive list of possible explanations beyond squelching as part of the revision.

We will discuss the difference in receptor levels between the cell lines, the different number of genomic GR binding sites and its possible implication in the observed residual binding after wash-out in U2OS-GR cells as suggested.

We agree that the coverage plots do not take the fraction of binding sites with signal into account. However, by also showing the heat maps, this information is also available to the reader. In our opinion, the coverage plots provide a straight-forward way to compare the signal for the different categories of peaks. The violin plots are an interesting alternative way to present the data, which also captures the diversity in the signal within each group. We will add violin plots to the supplementary data as requested.

We see your point. However, based on the ATAC-signal (Fig. 5D) the changes in nucleosomal occupancy upon GC treatment are the same for naiive and primed cells and revert to their base-line level after hormone withdrawal. This indicates that these loci have comparable nucleosome occupancy after wash-out. Yet, the levels for these histone modifications do not differ between primed and naiive cells indicating that these histone marks do not “mark” the promoter of primed genes after wash-out.

We are reluctant to put p-values on every chart, especially for experiments with few replicates. Importantly, we always plot the values for each individual data point, so the reader can gage if they differ between conditions. We will add p-values for figure 4 to test (support) our claim that ZBTB16 is primed whereas other GR target genes are not.

A similar suggestion was brought up by reviewer #1, here is the response we gave to this comment: When compared to FKBP5, ZBTB16 indeed has very low levels of pre-hormone expression. However, this is unlikely to explain the observed “memory” for ZBTB16 given that there are other genes with similarly low pre-hormone levels that do not show more robust responses upon repeated hormone exposure (see Fig. 3B,D). For the FISH experiments, we decided to include a non-primed gene (FKBP5 as control). We agree that adding additional control genes with comparable basemean levels would be informative. For example, this would tell us if a response of only a subset of cells in the population to hormone is specific to ZBTB16. Based on single cell studies by others (PMID: 32170217), most GR target genes show a response in only a subset of cells indicating that this is unlikely a unique feature of ZBTB16 explaining the priming observed. Rather than performing additional experiments, we will revise the discussion to acknowledge the difference in basemean and the potential role of cell-to-cell variability in explaining the observed “memory” for the ZBTB16 gene.

The fact that we do not observe elevated expression of other genes upon repeated expression could be due to the relatively short length of the hormone treatment, 4 hours, which was chosen to enrich for direct target genes of GR. These four hours might be insufficient for transcription, translation and ultimately gene regulation by the ZBTB16 protein. We have not looked at ZBTB16 protein levels.

**Minor Comments**

We will include this information in a revised version of the manuscript.

We will add the requested peak-centric view. Based on a previous study (PMID: 29385519), we expect that binding is a poor predictor of gene regulation of nearby genes, especially for repressed genes.

In our analysis, we looked at opening and closing peaks independently. If a peak is in the vicinity of multiple genes, it will only be assigned to the closest one. Thus, genes that have both and opening and a closing peak in the 50kb window will be included in both the analysis of closing sites and opening sites. We have not looked at clusters of binding sites, but agree that this would be interesting to see if the combinatorial action of multiple peaks makes regulation of the gene more likely. We will look into this during the revision process.

1. The authors claim on p10 that "We could validate several examples of opening and closing sites and noticed that opening sites are often GR-occupied whereas closing sites are not occupied by GR". As most of the ChIP-Seq experiments were performed on formaldehyde-only fixed cells, the authors might miss "tethered" sides, which are mostly linked to gene repression. You might rephrase this part to most closing sites lack direct DNA binding.

Even though several studies indicate that tethered binding can be captured using formaldehyde-only fixed cells (e.g. PMID: 32619221, PMID: 15879558), we agree that the ChIP-assay might have blind spots, for instance for tethered binding, and will revise our statements as suggested.

This might be related to comment #4 given that P300 is brought to the DNA by other transcription factors whereas H3K27ac is directly DNA-bound which likely influences the cross-linking efficiency. By resorting the heat-maps, we will be able to determine the overlap between p300 recruitment and changes in H3K27ac levels (the other main enzyme that deposits this mark is CREBBP (a.k.a. CBP)).

We will include this information in a revised version of the manuscript.

We have not looked into this but a previous study by the Reddy lab (PMID: 22801371) has investigated binding sites in A549 cells that are occupied at very low Dex concentrations. They found that this is not driven by a specific GR motif but rather by the presence of binding sites for other transcription factors and chromatin accessibility.

This data for the GILZ gene is shown in Figure S2C. When we revise the manuscript we will add this information to main figures 1 and 2 as suggested.

This is shown in figure S3C and shows that expression levels of certain genes (ZBTB16 and FKBP5 but not GILZ) stay high after Dex washout (but not cortisol wash-out) consistent with persistent GR binding at a subset of GR-occupied loci for the experiments using Dex.

For both S2C and S3C, cells were treated for 4h with Dex before the wash-out. For the ZBTB16 and FKBP5 genes, the persistent GR binding after wash-out is accompanied by a preserved Dex response after wash-out. For GILZ, GR binding at one of the peaks near the GILZ gene is also preserved, yet the expression of this gene reverses to its pre-treatment levels after wash-out. A possible explanation is that the residual binding at the GILZ gene is observed for only one of several nearby GR peaks. Previous studies, where we deleted GR binding sites near the GILZ gene, have shown that the combined action of multiple GR-occupied regions is needed for robust induction of this gene (PMID: 29385519).

A trivial explanation for the overlaying H3K27ac and H3K27me3 marks at the ZBTB16 locus is that the ChIP data represents a population average. From our single-cell FISH experiments, we found that only a subset of cells activates ZBTB16expression upon hormone treatment so a potential explanation is that the cells of the population that respond are responsible for the H3K27ac signal whereas the non-responders are decorated with H3K27me3. We will include this information in a revised discussion. On a single histone, H3K27me3 and H3K27ac are mutually exclusive. However, given that a nucleosome has 2 copies of histone H3, both modifications can in principle co-exist.

We’re guessing here, but we assume the reviewer refers to the potentially slightly higher H3K27me3 levels upon Dex treatment for ChIP-seq whereas the qPCR indicates that the levels do not change? The change seen in the ChIP-seq experiment is marginal and based on a single experiment. In contrast, the qPCR data shows the results from three biological replicates and therefore is probably a more reliable source of information.

We will include this information in a revised version of the manuscript.

Cancer cell lines often have variable karyotypes and our FISH data suggests that the ZBTB16 locus is present in more than 2 copies in some of the A549 cells. Here’s the info from the ATCC website describing the karyotype of A549 cells: …” This is a hypotriploid human cell line with the modal chromosome number of 66, occurring in 24% of cells. Cells with 64 (22%), 65, and 67 chromosome counts also occurred at relatively high frequencies; the rate with higher ploidies was low at 0.4%.....”.

Upon quick inspection, we find that GR target genes are typically not marked by H3K27me3, however ZBTB16 does not appear to be the only one. When we revise the manuscript, we will look more systematically at the link between gene regulation by GR and genes marked by H3K27me3 to determine how “special” the presence of this mark is, which will also inform us about the likelihood that it is linked to the transcriptional memory observed for the ZBTB16 gene.

We are not sure if ZBTB16 regulation by GR is tissue independent. However, in contrast to most GR target genes that are regulated in a cell-type-specific manner, ZBTB16 is regulated in both cell lines we examined and has also been reported to be a GR target gene in other cell types e.g. in macrophages (PMID: 30809020).

Reviewer #3 **Major Comments:**

For sure the washout time matters and we do not doubt that the persistent changes observed upon shorter wash-out by the Hager lab are real. One of the reasons we chose the 24h period was to see if the changes observed by Lightman and Hager might persist for extended periods of time as suggested by Zaret and Yamamoto. Our findings suggest that this is not the case and that the majority of GR-induced changes are short-lived. Perhaps future studies can shed light on how long changes persist. However, given the slow dissociation between GR and Dex, we expect that it might be hard to dissect if persistent changes are indeed persisting in the absence of GR binding or reflect an incomplete hormone wash-out.

The objective of this study was to find out if persistent changes as observed in Ref33 are the exception or the rule not to test if the original observation is correct (importantly, another cell line was used in Ref33 which makes a 1:1 comparison impossible to begin with). We believe that we have convincingly shown that, for the cell lines we assayed, persistent changes are rare if occurring at al. Given that no convincing persistent changes were observed after a 24h washout, we think that it is very unlikely that such changes would be observable after even longer wash-out periods. We do not intend to include experiments using longer wash-out but will revise the discussion to emphasize that the lack of persistent changes we found might be specific to the cell lines we chose for our studies.

We agree that adding this percentage is a good idea as this would allow for a more quantitative comparison between the different groups. Here are the numbers:

A549 cells:

opening sites: 49%

closing: 10%

nonchanging: 18%

U2OS cells:

opening: 54%

closing: 0.2%

nonchanging: 7%

We will include this information in a revised version of the manuscript.

For the ATAC-seq experiments, we treated the dex-treated and cort-treated experiments as replicates to find candidate regions with persistent chromatin changes. For the ATAC-seq data, a site is 'persistent' if called (by MACS2, e.g. DEX vs EtOH) upon treatment and then again 24h after washout (DEX washout vs EtOH washout). For the ATAC-qPCR experiments, we performed 4 biological replicates and will perform a t-test to determine if the small difference we observe at some sites between the EtOH and washout is statistically significant. Given the overlapping error bars and the very small difference, don’t expect the difference to be significant even for these most promising candidates from our genome-wide analysis.

Indeed we did not find a mechanistic explanation for the ZBTB16-specific memory. Possible explanations are discussion in the following section of the results (page 14-15): “… Mirroring what we say in terms of chromatin accessibility, transcriptional responses also seem universally reversable with no indication of priming-related changes in the transcriptional response to a repeated exposure to GC for any gene with the exception of ZBTB16. Although several changes in the chromatin state occurred at the ZBTB16 locus, none of these changes persisted after hormone washout arguing against a role in transcriptional memory at this locus (Fig. 5). Similarly, the increased long-range contact frequency between the ZBTB16 promoter region and a GR-occupied enhancer does not persist after washout (Fig. 5e). Notably, our RNA FISH data showed that ZBTB16 is only transcribed in a subset of cells, hence, it is possible that persistent epigenetic changes occurring at the ZBTB16 locus also only occur in a small subset of cells and could thus be masked by bulk methods such as ChIP-seq or ATAC-seq. Another mechanism underlying the priming of the ZBTB16 gene could be a persistent global decompaction of the chromatin as was shown for the FKBP5 locus upon GR activation [35]. Likewise, sustained chromosomal rearrangements, which we may not capture by 4C-seq, could occur at the ZBTB16 locus and affect the transcriptional response to a subsequent GC exposure. Furthermore, prolonged exposure to GCs (several days) can induce stable DNA demethylation as was shown for the tyrosine aminotransferase (Tat) gene [71]. The demethylation persisted for weeks after washout and after the priming, activation of the Tat gene was both faster and more robust when cells were exposed to GCs again [71]. Interestingly, long-term (2 weeks) exposure to GCs in trabecular meshwork cells induces demethylation of the ZBTB16 locus raising the possibility that it may be involved in priming of the ZBTB16 gene [72]. However, it should be noted that our treatment time (4 hours) is much shorter. Finally, enhanced ZBTB16 activation upon a second hormone exposure might be the result of a changed protein composition in the cytoplasm following the first hormone treatment. In this scenario, increased levels of a cofactor produced in response to the first GC treatment would still be present at higher levels and facilitate a more robust activation of ZBTB16 upon a subsequent hormone exposure. Although several studies have reported gene-specific cofactor requirements [73], the 14 fact that we only observe priming for the ZBTB16 gene would make this an extreme case where only a single gene is affected by changes in cofactor levels……”.

**Minor Comments**

We will include a motif analysis for opening and closing sites in a revised version of the manuscript.

We will revise the label in a revised version of the manuscript as suggested.

We actually prefer the MA plots as they also provide information regarding the basemean counts for regulated genes. This allows one, for example, to see that other GR-regulated genes with similar basemean counts do not show a “memory” suggesting that the low expression level for ZBTB16 likely does not explain the observed priming.

We will include this information in a revised version of the figure.

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Referee #3

Evidence, reproducibility and clarity

Summary:

In this study, Bothe et al investigated the functional role of glucocorticoids on gene regulation and chromatin accessibility using ATAC-seq, RNA-seq data in A549 and U2OS-GR cells under different conditions. They focused on transcriptional memory of GR activation, meaning a more robust transcriptional response upon repeated hormone stimulation (transcriptional memory). A previous study reported persistent changes after more than 9 days, but here the authors focused on a 24-hour washout period which they reasoned would be more likely to reveal persistent changes. However, they found that only identified a single gene, ZBTB16, with this characteristic. The studies are well performed, but the reader is left confused as to whether the difference between the present and previous result is a timing issue. That needs to be addressed. In parallel, the authors found that chromatin accessibility was also reversible after hormone withdrawal. This was also true for the ZBTB16 gene and thus could not explain the transcriptional memory for this gene. The authors suggest that priming increases ZBTB16 output by increasing the fraction of cells responding to hormone treatment as well as by augmenting activation by individual cells. This is interesting, but the reason why the ZBTB16 gene is special is not explained. Moreover, since ZBTB16 was the only gene where hormone-induced changes were not reversible, the conclusion that "hormone can induce gene-specific changes in the response to subsequent exposures which may play a role in habituation to stressors and changes in glucocorticoid sensitivity" seems an overstatement especially since the title states that changes are universally reversible. Also the discussion ends by arguing that it is still likely that individual cells remember previous hormone exposure, even though the present paper argues strongly against that except for a single gene where the mechanism of the memory is completely unclear. This discrepancy between what "might be the case" and what the authors actually observe needs to be corrected.

Major Comments:

1. Although the authors reported that only ZBTB16 displayed transcriptional memory, would more genes emerge with less stringent cutoffs, for example Fold Change> 1.5 & adjusted p value < 0.05?
2. One question the authors should consider is whether the washout time matters. What if it were reduced to a shorter time, for example 8 or 12 hrs? This might especially alter the conclusions about dexamethasone, which Lightman and Hager have suggested to have a long half life of binding to the GR in cells.
3. The authors point out that Ref. 33 focused on persistent changes after more than 9 days, but the authors state that they focused on a 24-hour washout period which they reasoned would be more likely to reveal persistent changes. However, that was not the case, and the present findings seem to be at odds with the conclusion drawn in Ref. 33. This begs the question of whether the original report was correct and authors would have seen persistent changes (by whatever mechanism) after 9 days, or whether there almost no persistent changes at all as the present study would suggest. To address this and advance the field on this point, it is imperative that the authors do the "positive control" of repeating the protocol used in the original report, to determine if the difference is quantitative (timing) or qualitative (true discrepancy between two groups).
4. The authors state that "opening sites are often GR-occupied whereas closing sites are not occupied by GR" in Figs 1B and C. What is the fraction of opening sites with GR binding?
5. In Fig. 2C the authors show SLC9A8 as an example of a gene which maintained a reduced level of open chromatin when assessed by ATAC-seq. To "validate" this they performed ATAC-PCR, and in the results shown in Fig. 2D any differences were not found to be statistically significant. However, these are two different assays, and both have potential flaws and experimental error. Were biological replicates of ATAC-PCR performed, and if so were the differences in ATAC-seq signal between EtOH and washout statistically significant? And is this true of other genes with similar patterns, such as FKBP5, PTK2B, and others?
6. The authors suggest that priming increases ZBTB16 output by increasing the fraction cells responding to hormone treatment, but no explanation was found to explain why this happens to ZBTB16 but not all of the other GC-induced genes. This needs to be discussed.

Minor Comments

1. What motifs are enriched at the ATAC sites that open and close?
2. Fig. 1F would be improved by rephrasing the labels using terms "without site/peak" and "with site/peak". Otherwise, readers may think they are all GR peaks.
3. For Figs. 3B-3D, volcano plots are a better way to present the differentially expressed genes.
4. p values should be shown in Figs. 6C, 6D, 6F and 6G.

Significance

This is important since glucocorticoids are important hormones and drugs. A limitation of this study is that it's all in cell lines. One concern is that the conclusions differ from those in reference 33 and that will minimize the significance unless this is addressed by the authors, for example by using the 9 day protocol that was used in ref 33 to determine if those results are reproducible.

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Referee #2

Evidence, reproducibility and clarity

Summary

Bothe and colleagues studied the effect of repeated glucocorticoid exposure on DNA accessibility and gene expression in A549 and U2OS-GR cells and show that most of the glucocorticoid receptor (GR) induced changes are reversible in both cell lines and after long-term (20 hrs) and short-time (4 hrs) dexamethasone (Dex) or cortisone treatment. They identified a single gene that seem to have persisting memory of previous Dex exposure, namely ZBTB16.

Major Comments

1. The authors used the cancer cell lines A549 and U2OS-GR as model systems the latter additionally overexpresses GR. In order to make the work more translatable an in-vivo model comparing the effect of long-term, short-term and repeated glucocorticoid (GC) treatment on DNA accessibility and gene expression is necessary. The authors should clearly emphasizes this limitation of their study in the discussion or add in-vivo data (e.g. qPCRs) to strengthen the translatability.
2. The authors draw conclusions of the association of DNA accessibility, H3K27ac, P300 and GR occupancy from independent heatmaps. This cannot be easily done from the current way the data is presented. A direct link between accessibility, H3K27ac and mRNA expression of the associated gene for example is missing. a.) The authors show several heatmaps to indicate changes in accessibility, H3K27ac and P300 upon Dex treatment as well as GR binding patterns in Fig. 1 and S1. Those are sorted by decreasing signal strength (I assume). To make those results more comparable, I suggest to sort them all in the same way (e.g. by descending ATAC-Seq signal or fold-change). b.) In line with a.), it is unclear to the reader if those sides opening /closing are the same sides showing increased/decreased H3K27ac or P300 occupancy and if those sides bind GR. Integrating this data together with mRNA e.g as correlation plots would strengthen the author's argument that accessibility, H3K27ac and mRNA changes are indeed correlated. What about the GR binding sites that do not change accessibility or H3K27ac? What makes those different? Therefore, the statement "Furthermore, closing peaks, which show GC-induced loss of H3K27ac levels and lack GR occupancy (Fig. S1c-f), were enriched near repressed genes" on page 10 as well as the statement "suggesting that transcriptional repression by GR does not require nearby GR binding." in the abstract and discussion cannot be made from how the data is presented. c.) Several recent studies have shown that GR's effect on gene expression and chromatin modification at enhancers might be locus-/context-specific ("tethering", competition, composite DNA binding) and/or recruitment of different co-regulators (see Sacta et al. 2018 (doi: 10.7554/eLife.34864), Gupte et al. 2013 (doi.org/10.1073/pnas.1309898110) and many more). Defining the GR-bound or opening/closing sides in terms of changing H3K27ac (or having H3K27ac or not) more closely would help to link those to gene expression changes e.g. in violin plots. Furthermore, the authors could include a motif analysis to see if the different enhancer behaviours can be explained by differences in the GR motif sequence or co-occurring motifs. Thereby more closely defining the mechanism of chromatin closure a sites that lack GR binding e.g. by displacement of other transcription factors as described for p65 in macrophages (Oh et al. 2017 (doi.org/10.1016/j.immuni.2017.07.012)). In general a more detailed analysis of the data is required before the authors could state "Instead, our data support a 'squelching model' whereby repression is driven by a redistribution of cofactors away from enhancers near repressed genes that become less accessible upon GC treatment yet lack GR occupancy." on page 10. The results might also be explained by competitive transcription factor binding, tethering or selective co-regulator recruitment (e.g. HDACs).
3. The authors use U2OS-GRa cells as a second cell line. Those cells overexpress rat GRa (see DOI: 10.1128/mcb.17.6.3181) in a cell line that usually does not express GR. I am wondering to what extend the overexpression reflects residence times and GR binding kinetics of cells endogenously expressing GR (mostly to at a lower protein level). At least the number of GR binding sites as well as the number of opening chromatin sites is much higher in U2OS-GR cells the A549 cells. The authors should discuss this point with respect to the observed preservation of some GR-binding sites U2OS-GR cells after Dex treatment and washout.
4. In figure 1 and S1, the authors show coverage plots on top of the heatmaps to show the mean signal in ATAC-Seq, GR, H3K27ac or GR signal between the different subset. These plots are statistically inappropriate as a significant portion of the enhancers does not have a signal and a few enhancers show a very strong signal (at least for H3K27ac, P300 and GR) which skews the mean. Plotting the signal distribution or the distribution of the Dex-dependent change in signal (fold-change, e.g. as violin plots) more accurately reflects the diversity in the signal response.
5. ChIP qPCRs against histone marks in figures 5B and S2C are not normalized for histone H3, but the author's clearly see changes in nucleosomal occupancy at those sides by ATAC-Seq. Additional normalization by total H3 is highly recommended.
6. Figures 1C, 2D, 4A/B, 5B/C/E, 6C/F, S2C/E and S3A-D lack statistics.
7. In figure 6, the authors compare the ZBTB16 locus with FKBP5, a locus that as by the data presented is very different from the ZBTB16 locus in terms of expression level (Fig 6C/F) and H3K27me3 occupancy (Fig. 5B). The authors should compare ZBTB16 to a locus with similar expression level and H3K27me3 deposition. Especially the co-occurrence of H3K27me3 and H3K4me3 (Fig. 5B) at the ZBTB16 promoter indicates its poised chromatin state whereas the FKBP5 promoter is marked by an active chromatin state.
8. ZBTB16 itself is a transcriptional regulator, but its elevated expression upon repeated Dex treatment does not affect other genes. How do the authors explain this observation? Is ZBTB16 elevated on the protein level as well?

Minor Comments

1. The authors nicely explained the data analysis of their ATAC-Seq data, I recommend to include some more information on if and how the ChIP-Seq data was normalized (library size, scaling factors or spike-ins) even if most of the data sets are published.
2. In figures 1F and S1F, the authors show the association of opening/closing an non-changing sites and GR peaks with genes that are up/down-regulated or unchanged upon Dex treatment. This gene-centric analysis is skewed by the different sizes of up-/down regulated gene sets and opening/closing chromatin (especially for the U2OS-GR cells that have 15.6x more opening sites then closing sites). Could the authors also include a peak-centric view showing how many closing/opening and non-changing sites are associated with down/up-regulated or unchanged genes? How good is the association (correlation)?
3. In the figures 1F and S1F it is unclear how the authors handled genes with associated peaks (within +/-50kb) that show different characteristics e.g. a gene with a peak that gains and another peak that loses accessibility. How do the authors account for >1 opening or closing peaks per gene? In relation to this. Do opening/closing sites cluster around up/down-regulated genes? What is the stoichiometry as 1.6x more closing sites (then opening sites) relate to 1/3 of repressed when compared to activated genes?
4. The authors claim on p10 that "We could validate several examples of opening and closing sites and noticed that opening sites are often GR-occupied whereas closing sites are not occupied by GR". As most of the ChIP-Seq experiments were performed on formaldehyde-only fixed cells, the authors might miss "tethered" sides, which are mostly linked to gene repression. You might rephrase this part to most closing sites lack direct DNA binding.
5. The P300 ChIP-Seq in Fig S1B shows less sides with P300 occupancy then sides with H3K27ac. Is this a ChIP quality issue or do other factors mediated changes in H3K27ac? Similar to mayor comment 1a, are the P300 sites on the top the same sites as the top H3K27ac sites?
6. Please indicate the primer position of qPCR primers if the genome browser tracks are displayed. That makes the comparison of sequencing and qPCR results easier.
7. The authors nicely show that GR binding sites with persisting accessibility after Dex treatment and washout in U2OS-GR cells show residual GR binding and are bound by GR at Dex concentrations of 0.1nM. Could the authors specify if differences in the GR motif exist between those and the non-persisting sites?
8. The authors focus on ZBTB16, FKBP5 and GILZ to show the priming effect of glucocorticoid treatment on ZBTB16 (Fig. 4), but GILZ was not included in the initial ATAC-Seq (Fig. 1) and ATAC-Seq washout (Fig. 2) experiments. For better comparison, I recommend adding qPCR results on GILZ in figures 1 and 2.
9. The authors indicate that the washout of Dex does restore gene expression in A549 cells to pre-Dex levels (Fig. 4). These cells did not show any persisting GR binding, so. How does the gene expression in U2OS cells behave? E.g. for the genes displayed in Fig. S2C.
10. In Fig. S3C, the authors observe that Gilz expression in U2OS-GR cells is similarly induced upon 1st and 2nd stimulation with Dex using 4hrs treatment. How does this relate to the preserved Dex response after 20hrs treatment and washout (Fig. S2C)? Was the expression of GILZ altered after 20hrs (see comment 9)? Are H3K27ac and GR signal after 4hrs Dex stimulation and washout comparable as well? Please comment on the differences observed between the 20hrs and 4hrs experiments.
11. The GR enhancer of ZBTB16 seems to be simultaneously marked H3K27ac and H3K27me3 (Fig. 5A). Please comment. Is this an artefact of bulk ChIP-Seq? Is this due to the different timings (H3K27me3 after 1h and H3K27ac after 3hrs)? Can both marks co-exists or do they reflect allelic differences?
12. Please comment on the observed differences in H3K27me3 response to Dex between ChIP-Seq (Fig. 5A) and the ChIP qPCR (Fig. 5B). Is this a timing issue?
13. Please indicate the number of replicates for the ChIP-Seq experiments in the figure legends.
14. The statement "Upon hormone treatment, both the number of transcripts per cell and the number of transcriptional foci increases." on page 13 is confusing. Most cells only have two alleles (max. two transcription foci). Is ZBTB16 duplicated in A549 cells?
15. ZBTB16 is marked by H3K27me3 (Fig. 5A/B). How many GR binding sites do overlap H3K27me3 in A549 cells? How many genes associated with GR/H3K27me3 sites are expressed in A549 cells? Is ZBTB16 the only one?
16. Is ZBTB16 a GR target gene that is regulated by GR tissue-independently (like GILZ and FKBP5)?

Significance

The work is of significant interest as glucocorticoids (GCs) are physiologically secreted with circadian and ultradian rhythms, but widely prescribed with repeated dosing during the day (in order to maintain high GC levels) in patients during chemotherapy (doi: 10.1016/j.critrevonc.2018.04.002, doi: 10.1186/1471-2407-8-84 ) or anti-inflammatory therapy in rheumatoid arthritis (doi: 10.1186/ar4686, doi:10.1093/rheumatology/kes086) for example. Therefore the assessment of long-term versus short-term as well as the effect of repeated GC exposure on various cell types is of high interest to understand adverse effects of GC therapy. However, the choice of cell lines as model system dampens the overall translatability of the findings, as does the choice of those cell lines. Alveolar epithelial cells (A549) are not classically known as a cell type affected by GC side effects in therapy. However, GR is widely known to regulate tissue-specific gene programs (doi: 10.1038/emboj.2013.106, doi: 10.1016/j.steroids.2016.05.003, doi: 10.1016/j.molcel.2011.06.016). Hepatic, skeletal muscle cells or fat cells would reflect those tissues more accurately. Obtaining in-vivo data is hampered by the cofounding effect of endogenous glucocorticoids and their circadian expression (doi: 10.1016/j.molcel.2019.10.007 ), but primary cells would overcome those limitations and still be a closer model system the cancer cell lines.

That the glucocorticoid receptor mostly binds accessible genomic regions and changes the DNA accessibility of a subset of binding sites after short-term treatment with Dex was previously described (doi: 10.7554/eLife.35073, doi: 10.1093/nar/gkx1044, doi: 10.1038/ng.759 ), but the reversibility of these effects were not studied before. Therefore, this study adds an interesting conceptual finding.

The observation that ZBTB16 expression can be boosted by repeated Dex treatment is interesting and seems to be tissue independent. Again, in-vivo or patient data confirming this observation would strengthen the conclusions from this paper and exclude an artefact from immortalized (cancer) cell lines. The impact of this observation depends on ZBTB16 function and if ZBTB16 is elevated on the protein level as well.

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Referee #1

Evidence, reproducibility and clarity

Bothe et al investigated whether GR induced chromatin changes could be somehow preserved after inactivation of the receptor. They performed ATAC-seq to examine the status of chromatin accessibility under several treatment conditions in two different human cell lines. Their main finding is that GR changes to chromatin are universally reversable, with the exception of a tissue-specific single locus (ZBTB16). Additionally, the authors claim their data support a squelching mechanism for transcriptional repression by GR.

Major comments:

Are the key conclusions convincing? Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation. Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments. Are the data and the methods presented in such a way that they can be reproduced? Are the experiments adequately replicated and statistical analysis adequate?

The manuscript is very well written. The data is clearly presented. The methods are explained in sufficient detail with a few exceptions mentioned below, and statistical analysis are adequate. There are some concerns and suggestions about the experimental design and data presentation.

• Drug treatments. It is not clear whether the cells were previously grown on charcoal-stripped serum before hormone treatments. From methods, it seems they were grown in 5% FBS and directly treated with the hormones. Also, what "hormone-free medium" mean? Is it charcoal stripped Serum or not Serum at all? Replicates for these data sets? The ATAC and Chip-Seq should have at least 2. The concordance of the ATAC-seq and Chip-seq replicates should be described and shown in supplemental figures. Fig1A - The ATAC-seq HM should be clustered to show which peaks in opening/closing and unchanged peaks also have called GR chip peaks. Showing browser shots as in Fig1B is cherry picking data and can be put in a supplementary figure as an example. This is a main point of emphasis of the manuscript so show the data. The atac peaks that do overlap with GR chip peaks should be sorted by GR peak intensity. The QPCR is then only needed to confirm the quantitative changes.

To show both the ATAC sites and H3K27ac sites are specific to hormone treatment, a random set of 15K peaks not in this peak set also should be shown in HMs and should not change with the treatments. Why does the H3K27ac go down in the 6768 non changing sites with dex?

The D & E parts of Fig1 can then be eliminated to become parts of Fig1A. Its not clear in the text that the HMs in Fig1 are all sorted in the same way.

• Fig. 1b (and d). The ChIP data is from 3h-hormone treatment while the ATAC-seq data is from a 20h hormone treatment. It seems a bit misleading to directly compare GR occupancy with the state of the chromatin at different time windows. Shouldn't the authors show their ATAC-seq 4h treatment data (shown in Fig S1) here instead?
• Fig. 1f. The authors sate "downregulated genes only show a modest enrichment of GR peaks". However, there is a significant enrichment of GR-peaks in repressive genes compared to non-regulated genes. It would be interesting to see how some of these peaks look in a browser shot. While the general conclusion "transcriptional repression, in general, does not require nearby GR binding", seems valid, the observation that many GR peaks appear directly bound to nearby repressed genes ought to be more emphatically recognized in the text.
• Concept of naïve cells (Fig. 3A). If cells are normally grown in serum-containing media, which is known to have some level of steroids, can the cells described here as "Basal expression" be truly free of a primed state? In the first part of the experimental design (+/- 4h hormone), which type of media is present here? Is it 5% FBS? A concern is that the authors may require the assumption that the (4h + 24h) period a is sufficient to erase all memory of the cells, which is exactly what they are trying to test.

The transcriptional memory is a second major emphasis of the paper.

The RNA primers (Table 1) span within an exon or across 2 exons to best measure mRNA levels. The QPCR primers should span exon intron boundaries to better reflect transcriptional activity (prior to mRNA splicing) at the collection time point.

It would be interesting to do a time course of the hormone-free period of the washout to determine the memory of the chromatin environment that results in the enhanced transcriptional response instead of just 24 and 48 hrs in A549 cells.

Fig 5A appears to show H3K27ac overlaying H3K27me marks near the promoter of ZBTB16 and at the GR sites within the gene locus with no reduction in H3K27me levels. This seems counterintuitive and should be explained or addressed especially since the authors use quantitative comparisons of H3K27ac levels with and without treatment in other figures.

Showing the changes of ZBTB16 upon 2nd stimulation via FISH is not terribly surprising and is even the most expected reason for higher RNA levels. Why does it only occur at that gene is a better question and is touched on in the discussion. It is more likely that this gene has a very low level of pre-hormone transcription compared to FKBP5 (see Fig 3e and the FISH images). ZBTB16 is in the lower 3rd of basemean RNA levels of GR responsive genes according to the RNAseq data. Selection of 1 or 2 other genes with similar basemean levels of RNA (from the RNA-Seq data) would make the data more

Minor comments:

Specific experimental issues that are easily addressable. Are prior studies referenced appropriately? Are the text and Figures clear and accurate? Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

• In the Intro (paragraph two), the authors explain the different mechanisms by which GR might repress genes. One alternative the authors appear to have missed is the possibility of direct binding to GREs while, for example, recruiting a selective corepressor such as GRIP1 (Syed et al., 2020). There are many recent critics to the notion that transrepression via tethering is responsible for GR repressive actions at all (Escoter-Torres et al., 2020; Hudson et al., 2018; Weikum et al., 2017).
• When the authors introduce the concept of tethering to AP-1, they go way back to the first description of tethering. However, one of the references (Ref 20) actually goes against the tethering model as they did not detect protein-protein interactions between AP-1 and GR, and also, they conclude that repression requires the DNA-binding domain. -Figure 2. The authors state "This suggests that the few sites with persistent opening are likely a simple consequence of an incomplete hormone washout and associated residual GR binding". The authors should check the subcellular distribution of GR after their washout protocol. If the washout is not completed, GR should still be in the nuclear compartment.
• The first part of the manuscript (Repression through "squelching") seems a bit disconnected from the rest of the results (reversibility in accessibility). The abstract is structured in a way that this disconnection seems much less obvious. Perhaps the authors could try to present their squelching part in the middle of the manuscript, following the flow of the abstract? This is just a suggestion.
• Figures have CAPS panel letters (A,B,C, etc) while the text calls for lower case letter (a,b,c...)

Escoter-Torres, L., Greulich, F., Quagliarini, F., Wierer, M., and Uhlenhaut, N.H. (2020). Anti-inflammatory functions of the glucocorticoid receptor require DNA binding. Nucleic Acids Res 48, 8393-8407. Hudson, W.H., Vera, I.M.S., Nwachukwu, J.C., Weikum, E.R., Herbst, A.G., Yang, Q., Bain, D.L., Nettles, K.W., Kojetin, D.J., and Ortlund, E.A. (2018). Cryptic glucocorticoid receptor-binding sites pervade genomic NF-kappaB response elements. Nat Commun 9, 1337. Syed, A.P., Greulich, F., Ansari, S.A., and Uhlenhaut, N.H. (2020). Anti-inflammatory glucocorticoid action: genomic insights and emerging concepts. Curr Opin Pharmacol 53, 35-44. Weikum, E.R., de Vera, I.M.S., Nwachukwu, J.C., Hudson, W.H., Nettles, K.W., Kojetin, D.J., and Ortlund, E.A. (2017). Tethering not required: the glucocorticoid receptor binds directly to activator protein-1 recognition motifs to repress inflammatory genes. Nucleic Acids Res 45, 8596-8608.

Significance

The study tackles two important questions. One is regarding the effects of inducible transcription factors on chromatin structure after inactivation. The second is on the mechanisms behind transcriptional repression.

The effect of GR inactivation on chromatin accessibility has already been addressed in previous work for a single locus (Refs 38) or genome wide (Ref 33). However, the 24h temporal windows have not been addressed before. In this sense, the manuscript sheds some new light into the matter. Even though the authors conclude that accessibility is globally reversable, they only studied in detail the mechanism behind a single-locus exception.

Regarding the mechanisms behind transcriptional repression, the authors present data supporting the squelching mechanism, which is still highly controversial.

The manuscript will be of interest to the molecular and cell biology communities, especially those working on chromatin structure, transcription factors, gene regulation, and nuclear receptors. Overall, this is an interesting paper with somewhat limited novel findings that is suitable for publication after addressing the above comments. The rigor of the findings needs to be better described via replicates and if they have not been done, it should be a major requirement of revision.

The reviewers specialize in transcription factor dynamics.

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Reply to the reviewers

We thank both reviewers for their comments on our manuscript. Our responses to their specific comments and plan to modify the manuscript are described bellow.

Response to reviewer #1

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> Figure 1C is difficult to interpret. Am I supposed to see anything in particular in the two insets? Please provide a descriptive interpretation of the inset and let the reader know if anything in particular is to be noted.

We agree that it is a bit difficult to interpret although the goal of these images is to show that spermatogenesis appears globally not disturbed until the histone-to-protamine transition in distorter males. We will change the legend of the figure to clarify this particular point.

> Figure 1D. Elsewhere, in supplemental S1, they have an image for SD5/CyO. This should be provided here as a control. As presented, the genetics don't prove that the interaction between SD5 and Gla is the cause of the phenotype. As presented in the figure, the effect could be caused by SD5 alone, independent of Gla. In S1, this is not the case - SD5 with CyO doesn't produce the phenotype. Likewise, I think they should provide the SD5/CyO image in S1A in Figure 1C.

We can add the images of the SD5/CyO genotype (currently in FigS1) in Fig1C (whole testis) and in Fig1D (single cyst). We also suggest to present in this figure the other distorter genotype cn bw/CyO (which is currently in Fig S1). However, because the modified figure is going to be too big, we also suggest to split Figure 1 in two Figures with Figure 2 presenting FISH results including all controls. In this case, we will remove the supplemental figure 1.

> Figure 1E. These images are the formal proof (especially for Gla/SD5 genotype) that the large Rsp array is on the chromosomes that seem destined for removal from the cyst. However, there is no control. The authors should provide FISH results for the genotypes Gla/CyO and, ideally, also cn1 bw1/Cyo.

We agree with reviewer #1 and will provide images of the Gla/CyO control and cn1 bw1/Cyo in a new Figure 2 as explained above.

> Figure 2. Keeping consistent with other figures, can the Gla/SD5 panel be in the middle?

Yes. We swapped the Gla/SD5 and cn bw/SD-Mad panels.

Also, shouldn't there be SD5/CyO in Figures 2, 3 and 4, to demonstrate that the phenotypes are the result of the interaction rather than just SD5? I am OK with providing just the cn 1 bw1/SD-Mad here alone, since it is simply contrasted with Gla/SD5.

We agree that it would be better to show also the SD5/CyO controls. However, we chose to show only one control (Gla/CyO) to make the figures easier to read. We thus suggest to provide all images of the SD5/CyO genotype in supplemental figures.

> Figure 3A. In the scheme, can you provide greater detail as to where F-Actin is expected?

The scheme was modified to clarify this point.

> Figure 3B. It is stated that there is a size difference in the nuclei for IC stage and greater variation in ProtB-GFP staining within bundles. Can there be an effort to quantify these observations?

It would be difficult to quantify ProtB-GFP signal intensity and nuclear size in IC stage cyst because nuclei are very close to each other. The best way would be to squash testes to spread spermatid nuclei but there might be a bias on nuclear size/shape due to the squashing procedure. In addition, on squashed preparations, it is difficult to be sure that the nuclei analyzed and compared belong to the same cyst. We agree that quantification would help to describe the phenotype better but we think that the best read-out of the different SD phenotypes is the quantification of number of abnormally compacted nuclei in seminal vesicles which is provided later in the manuscript.

> Figure S4. There doesn't appear to be the same phenotype for Gla/SD-Mad (DAPI, ProtB-GFP) in post-IC stage bundles compared to what is seen in 3C for Gla/SD-5. In particular, in figure 3, the defective nuclei seem to be trailing, but in S4, while the bundle appears disorganized, there doesn't appear to be the trailing nuclei. Is this difference real or is it just the result of a single picture contrast? Some clarification could be helpful.

Actually, the images that were shown on Figure 3C for Gla/SD5 post-IC probably show the SD5 nuclei of one cyst (the normal one) and the Rsp nuclei being eliminated from another cyst (these are trailing behind nuclei which are too far to be included in the same image). We thus changed the images for Gla/SD5 for an image which looks like the one shown for Gla/SD-5 genotype for clarity.

We did not mention this observation in the manuscript but we actually see cysts in which abnormally-shaped nuclei are trailing behind the normal nuclei and sometimes IC cones around the abnormally shaped nuclei seem to be stuck close to the normal nuclei which are already individualized. It might be possible that IC progression around abnormal nuclei is slowed down compared to normal nuclei. The difference could not reflect different phenotypes but more likely different states of a dynamic process.

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Response to reviewer #2

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Reviewer #2 had no specific comments.

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Referee #2

Evidence, reproducibility and clarity

SD is a multi-component system, where two major factors Sd (a truncation allele of RanGAP that mislocalizes) and Rsp, a satellite DNA (whose copy number determines sensitivity to RanGAP distorting allele).

This study by Herbette et al. provide cytological characterization of Drosophila SD (segregation distortor), a male meiotic drive system, focusing on the process of histone-to-protamine transition. By thoroughly studying multiple alleles of SD, they find that the mechanisms by which SD accomplishes segregation distortion are not uniform. In some cases, spermatogenesis is perturbed at the level of protamine incorporation and in other cases, mature sperm can be generated yet they exhibit distorted segregation.

In one combination Gla/SD5, histone elimination is delayed (never complete), whereas cn bw/SD-Mad exhibit normal timing in histone elimination/protamine incorporation, although these two combinations result in similar, severe degree of distortion. They further show that DNA compaction is incomplete in these SD alleles (again more severe in Gla/SD5 condition) by using dsDNA antibody. Interestingly, defective spermatids in Gla/SD5 combination never progress to sperm maturation and enter seminal vesicle, defective spermatids in cn bw/SD-Mad combination are capable of entering seminal vesicle, but likely fail to fertilize or develop after fertilization, resulting in distortion.

This is a well-done study and provides important insights into the mechanisms of segregation distortion in the Drosophila melanogaster SD system. The quality of data is high, and I don't have any major concerns on this manuscript. Of course, the exact mechanisms of how SDs drive (i.e. why Rsp(S) alleles fail to condense properly, and how it is related to the Rsp copy number) remains unclear, this study provides a significant step forward to tackle this fascinating phenomenon of segregation distortion.

Significance

This study provides important insights into the underlying mechanism of segregation distortion during D. melanogaster spermatogenesis. Segregation distortion is a fascinating phenomenon of significant interest in evolutionary biology. Thorough cytological characterization of spermatogenesis phenotype that leads to segregation distortion provides much needed information, and this study is a significant step forward to understand how meiotic drivers might exploit the system to distort segregation for their advantage.

Referees cross-commenting

I think I and reviewer #1 seems to be in good agreement. I don't have anything in particular to add. This is a nice paper.

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Referee #1

Evidence, reproducibility and clarity

This is a very nice paper that combine cytology and genetics to provide insight into the mechanism of segregation distortion in the Drosophila SD system. The conclusions are well supported with multiple different experiments from different in angles. By using different genetic backgrounds - their conclusion that Rsp abundance dictates distinct outcomes is well supported. My primary suggestion is that they include a few more controls and provide some additional quantitative analysis. In some cases, quantitative conclusions are made without sufficient support.

Specific Comments.

Figure 1C is difficult to interpret. Am I supposed to see anything in particular in the two insets? Please provide a descriptive interpretation of the inset and let the reader know if anything in particular is to be noted.

Figure 1D. Elsewhere, in supplemental S1, they have an image for SD5/CyO. This should be provided here as a control. As presented, the genetics don't prove that the interaction between SD5 and Gla is the cause of the phenotype. As presented in the figure, the effect could be caused by SD5 alone, independent of Gla. In S1, this is not the case - SD5 with Cyo doesn't produce the phenotype. Likewise, I think they should provide the SD5/CyO image in S1A in Figure 1C.

Figure 1E. These images are the formal proof (especially for Gla/SD5 genotype) that the large Rsp array is on the chromosomes that seem destined for removal from the cyst. However, there is no control. The authors should provide FISH results for the genotypes Gla/CyO and, ideally, also cn1 bw1/Cyo.

Figure 2. Keeping consistent with other figures, can the Gla/SD5 panel be in the middle? Also, shouldn't there be SD5/CyO in Figures 2, 3 and 4, to demonstrate that the phenotypes are the result of the interaction rather than just SD5? I am OK with providing just the cn 1 bw1/SD-Mad here alone, since it is simply contrasted with Gla/SD5.

Figure 3A. In the scheme, can you provide greater detail as to where F-Actin is expected?

Figure 3B. It is stated that there is a size difference in the nuclei for IC stage and greater variation in ProtoB-GFP staining within bundles. Can there be an effort to quantify these observations?

Figure S4. There doesn't appear to be the same phenotype for Gla/SD-Mad (DAPI, protoB-GFP) in post-IC stage bundles compared to what is seen in 3C for Gla/SD-5. In particular, in figure 3, the defective nuclei seem to be trailing, but in S4, while the bundle appears disorganized, there doesn't appear to be the trailing nuclei. Is this difference real or is it just the result of a single picture contrast? Some clarification could be helpful.

I think this is a nice paper and I enjoyed reading it very much. The combination of the genetics (different RSP alleles from nature and the different X chromosomes) with the cytology provide a very reasonable explanation for why different genotypes seem to yield different effects. It provides some reconciliation among previous studies.

Significance

I think it is very significant.

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Reply to the reviewers

We are grateful for the careful read and constructive comments provided by the 3 reviewers assigned to our manuscript. Each reviewer provided thoughtful and clearly structured comments that helped us to better clarify points or summarize results in the manuscript that they indicated were not presented clearly or completely. We have revised the manuscript to address the points raised by the reviewers, incorporating edits and additional text throughout the manuscript, figure legends, and supplemental materials. We feel the revised version of the manuscript is much improved as a result of the revisions in response to the reviewers.

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Referee #3

Evidence, reproducibility and clarity

Summary:

The authors demonstrate a powerful method utilizing mNGS of individual mosquitoes utilizing reference-free analysis. This allows researchers to combine the resulting datasets of mosquito identification, blood-meal source, microbiome, viral sequencing, etc. Such knowledge could be a useful tool in detecting and responding to transmission of mosquito-borne diseases that affect human or animal populations, even though the technology is currently likely too expensive for widespread use (as acknowledged by the authors).

Major Comments:

No major revisions requested.

The authors provide their detailed methodology, including code, allowing for replication by other groups.

Minor Comments:

The authors' discussion of using this technique in order to detect pathogens should be qualified regarding detection vs possible transmission. Detecting a virus in an engorged mosquito does not necessarily mean that said mosquito can transmit the virus, but may have simply acquired it from a recent blood meal. The same can be said of detecting a plant pathogen following a recent sugar meal.

From the methods, it seems that mosquitoes were not washed prior to processing. This may make it difficult to discriminate between internal and external microbiota as well as lead to cross-contamination of surface microbiota between mosquitoes collected in the same trap.

Significance

This work currently would be of interest to other research groups examining the co-occurence of pathogens, other microbiota, and blood meals for field collected mosquitoes. While of great potential application to public health surveillance, the current cost is likely prohibitive.

My field of expertise is virology and vector biology with minimal background in NGS.

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Referee #2

Evidence, reproducibility and clarity

Summary:

In this study, the authors utilized unbiased meta-transcriptomic in sequencing 148 diverse wild-caught mosquitoes (Aedes, Culex, and Culiseta ​mosquito species) collected in California, with main aim of detecting sequences of eukaryotic, prokaryotic and viral origin. Their results show that majority of their sequenced data assembled into contigs corresponding to viral genomes. In their data, 7.4 million viral reads clustered as +ssRNA viruses including ​Solemoviridae, Luteoviridae, Tombusviridae, Narnaviridae, Flaviviridae, Virgaviridae, and Filovirida​ whereas 2.25 million viral reads identified as -ssRNA viruses comprising of ​Peribunayviridae, Phasmaviridae, Phenuiviridae, Orthomyxoviridae, Chuviridae, Rhabdoviridae, and Ximnoviridae​. With 0.94 million viral reads, dsRNA viruses formed the third most abundant virus category with viruses under families ​Chrysoviridae, Totiviridae, Partitiviridae, and Reoviridae. Under the prokaryotic taxa, Wolbachia​ species was the dominant group, followed by other lower abundance bacterial taxa that includes Alphaproteobacteria, Gammaproteobacteria, Terrabacteria group, and Spirochaetes. Trypanosomatidae was the most dominant eukaryotic taxa, followed up by reads from ​Bilateria​ and Ecdysozoa taxa. Ultimately, this study demonstrates that single mosquito meta-transcriptomic analysis has potential in identifying vectors of human health significance, potent emerging pathogens being transmitted by them and their reservoirs all in one assay.

Major comments:

1.Are the key conclusions convincing? The conclusions are accurate.

2.Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? None. The study's results, discussion and conclusion are appropriate.

3.Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

As much as the authors describe the use of mNGS as a tool in validating mosquito species and providing an unbiased look at the vector-associated pathogens, it is still prudent for them to use qPCR to validate the obtained RNASeq data (e.g. validation of the viral sequences).

4.Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments. The outlined methodology is realistic.

5.Are the data and the methods presented in such a way that they can be reproduced? The methodology is reproducible.

6.Are the experiments adequately replicated and statistical analysis adequate? Yes

Minor comments:

1.Specific experimental issues that are easily addressable. qPCR validation the obtained RNASeq data should be conducted.

2.Are prior studies referenced appropriately? The recently publications about mosquito microbiome/virome should be added. (eg.  doi: 10.1128/mSystems.00640-20.)

3.Are the text and figures clear and accurate? The resolution for Fig 4, Fig 6, SFig 2, SFig 4, and SFig 5 is poor. The author should update them.

4.Do you have suggestions that would help the authors improve the presentation of their data and conclusions? (1)in the method section, the mosquito has been washed to avoid the contamination from the environment before RNA extraction? (2)most part of non-host reads are matched to the viruses (10.5M), however only few of them were belong to the prokaryotes, does it means mosquito carries more viruses than prokaryotes. (3)none of the mosquito-borne virus known to occur in California (eg. WNV, SLEV, WEEV, ) has been found in Table 1 for the virus detected with complete genome in this study. In contigs level, did the author detected any mosquito-borne virus known to occur in California. Since the mNGS is very sensitive and this study include large sample numbers, why no known mosquito-borne virus was detected in their study should be discussed.

Significance

1.Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. With the existential threat of emerging novel pathogens of global health concern, efficient and rapid public health surveillance strategies are crucial in monitoring and possibly averting such eventual calamities. Specifically, mosquitoes are widely diverse and are known to harbor and transmit various pathogenic agents to humans and animals. Thus, this rapid identification of relevant vector species, pathogens and their reservoirs in one assay is a promising and convenient aspect of surveillance in the public health sector.

2.Place the work in the context of the existing literature (provide references, where appropriate). Shi et al reported the first single mosquito viral metagenomics study, in which her and the team demonstrated the feasibility of using single mosquito for viral metagenomics, a methodology that has potential to provide much more precise virome profiles of mosquito populations. In the present study, the authors have gone a step higher by aiming to combine three objective points in single mosquito meta-transcriptomic, as described in brief in their abstract and the comprehensive methodology outline.

Reference: Shi, C., Beller, L., Deboutte, W. et al. Stable distinct core eukaryotic viromes in different mosquito species from Guadeloupe, using single mosquito viral metagenomics. Microbiome 7, 121 (2019). https://doi.org/10.1186/s40168-019-0734-2

3.State what audience might be interested in and influenced by the reported findings. The methodology and findings described in this manuscript are important in advancing the public health field of vector surveillance. The identification of relevant vector species, pathogens and their reservoirs in one assay is a promising and convenient aspect of surveillance.

4.Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

I am an Associate Professor at a research institute. My lab research work focuses on Arbovirology studies, more specifically vector surveillance of known and novel viruses associated with mosquitoes and ticks, mosquito-transcriptomic studies, mosquito viruses tropism studies and other related mosquito-virus interaction studies.

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Referee #1

Evidence, reproducibility and clarity

This is a very interesting and well designed study on mNGS of mosquitoes. The authors demonstrate that they can distill valuable information on the vector species, the source of the blood meals and the microbiome/virome using a simple experimental approach and using single mosquitoes. A highlight of the work is that the paper is very comprehensive with an overwhelming dataset and thoughtful analysis. It is a showcase how sequencing data from a relative compact number of mosquitoes specimens can be used to conduct sophisticated computational analysis leading to meaningful conclusions. The authors make a strong case for the power of mNGS of mosquitoes that may be applicable to other (invertebrate) species. Especially the phylogenetic analysis based on SNP distance without have reference genomes and the grouping of contigs by means of co-occurence in datasets is original. We feel that the work deserves to be published.

Significance

We have a number of comments that the authors may consider in further improving the quality of their manuscript:

What is the impact of this paper?

I think it is possible that the paper will have a decent impact on the mosquito arbovirus field, because it adequately shows the possibilities that individual mosquito sequencing can bring (e.g. co-occurrence analysis). It may shift the balance to doing more individual mosquito sequencing instead of pools. The paper is also very extensive in the analyses that it does on this very rich data set. Below, some suggestions are given for additional analysis, which should be interpreted as a compliment to the interesting data set acquired. It should however be noted that the ideas and approaches taken are not entirely new. Sequencing individual mosquitoes, co-occurrence analysis and metagenomic sequencing have been done before, although not to this extent and not in this field. Several novel possibilities:

1. An unbiased way to check if you have the correct mosquito species and the ability to detect subspecies. Using the genetic distance of the transcriptomes they have likely corrected the missed identification in some samples, where these calls had a logical mistake made. The fact that subspecies overlapped with the sites of capture is very interesting and confirms the relevance of looking at the genetic distance also within species.
2. Blood-meal analysis from sequence data. Here they can get to species level for 10 out of 40 blood-engorged mosquitoes. The idea is interesting, as you would be able to get a lot more information if you can determine blood-meal origin from RNA-seq data (as shown in this paper). However, I feel that in the current paper (and this may be intentional) they do not properly show that RNA-seq is an adequate alternative to DNA sequencing of the blood. To convince me, I would have liked to have these results compared to DNA sequencing and see how much overlap there is. I understand however that the choice was made not to do this, but I do have a small note for the information given now. It was mentioned that 1 contig with an LCA of vertebrates is enough for a 'blood-meal origin' call. I am however left to wonder how reliable is 1 read? Are there really no contigs with an LCA in vertebrates in the non blood-fed mosquitoes? Also, what do we think happened in the mosquitoes that were visibly bloodfed but nothing was found; any speculation?
3. The study of co-occurrence, although not novel, is a nice addition to the mosquito virome/microbiome determination field. Identifying novel segments and missed segments of viruses is very nice. I do however wonder: did it ever occur that co-occurrence finds a 'linked' fragment that was clearly wrong? Were some post-analyses done to check if the results make sense? It seems, especially because the paper elaborates on examples, that you need some follow-up. This is not problematic, but a nice addition to the paper would be (as is also described below) to mention which segments were added to viral genomes by co-occurrence and if some checks were done to verify these hits.
4. Being able to say something about differences in viruses within the same mosquito species is super interesting. Pools do not give the possibility to say something about profiles and prevalence and the large size (148 mosquitoes) allows to find interesting correlations.

What parts do you think are problematic?

1. We question the validity 'blood-meal calls' as outlined above.
2. In this study they use % of non-host reads as a measure for the abundance of a pathogen (see e.g. Figure 3). I don't understand this at all... If you have more pathogens, then the amount of non-host reads would have to go up right? It seems to assume that the amount of non-host reads you have is similar in all samples? It becomes even more problematic when the trend is mentioned that having a higher % of non-host reads for Wolbachia is related to a lower % of non-host reads for viruses. This seems to be trivial as the amount of non-host reads goes up with increased Wolbachia infection, and therefore the % of non-host reads for viruses goes down due to the larger denominator. A different number than 'non-host reads' should be taken to normalise the data and say something about abundance. E.g. host reads or spiked RNA?

What are the most relevant questions you are left with?

1. I am curious about the limited overlap with Sadeghi et al., 2018, who sequenced so many Culex mosquitoes in California. I would suggest to say a little but more about these discrepancies and their potential causes in the discussion.
2. What do the authors think are in those 'dark reads'? Is the amount of dark reads the same across the different samples? Similarly, are the 'tetrapoda' reads reduced/absent in mosquitoes with a reference genome available?
3. In the first part of the results, mention is made to being able to characterize to kingdom level 77% of the 13 million non-host reads (also see comment on non-host reads below). I am however puzzled with the description in the text and supplemental figure 3: which 3 million contigs were not able to be characterized? Where in supplemental figure 3 are they? This is especially puzzling as the main text mentions that 11 million non-host reads are from complete viral genomes, 0.9 million to eukaryotic taxa and 0.7 million to prokaryotic taxa?
4. There seem to be 131 bars, corresponding to individual mosquitoes, in figure 3? Where are the remaining 17?

What are your tips (in addition to responses to above questions)?

1. I think the definition of 'non-host reads' needs to be clearly made and used consistently across the document. At the end of the paragraph 'Comprehensive and quantitative analysis of non-host sequences detected in single mosquitoes' the concept of "...13 million non-host reads..." is introduced. At first glance of supplemental figure 3 it seems that "non-host reads" could also be defined as the 16.7 aligned reads that are left after putative host sequences are removed. Although it is true that the derivation of 13 million is explained in the figure text of supplemental figure 3, it may be easier for the reader (as it cost me some time) to explain this in the main text. In addition, is the definition of 'non-host reads' (corresponding to 13-million reads) corresponding to "classified non-host reads" in the following excerpt: "For every sample, "classified non-host reads" refer to those reads mapping to contigs that pass the above filtering, Hexapoda exclusion, and decontamination steps. "Non-host reads" refers to the classified non-host reads plus the reads passing host filtering which failed to assemble into contigs or assembled into a contig with only two reads."? This caused some confusion.
2. I believe it would be a valuable addition to add a table for the viruses which includes: 1) How it was determined that the complete genome is there, 2) The percentage overlap for those segments that were identified with blast and 3) Which viruses were already known.
3. Have the numbers of the caught mosquitoes somewhere written out in the materials and methods.
4. Pg2 L1-3: "Metagenomic sequencing..... a single assay." Perhaps a bit early for this statement. Would suggest to place it two paragraphs later before:"Here, we analyzed...."
5. Figure S4 is too pixelated to read. Perhaps due to pdf conversion, but please do check before submission.

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Reply to the reviewers

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

Many flatworm species reproduce asexually, by fission, and the process relies on the activity of stem cells (neoblast), which drive regeneration. The question that this work tries to address is what is the dynamics of stem cells in this process, including how many stem cells contribute to regeneration, what are the mutation rates and selection mechanisms, if any. Towards this, the authors tracked one specimen of planarian Girardia tigrina for more than ten rounds of fission, and re-sequenced its genome at multiple time points and applied methods of population genetics to analyze and model the data. The main conclusion of the work is that there is high somatic mutation rate, rapid loss of heterozygosity, and a small size of the stem cell population that contributes to regeneration after fission.

Reviewer #1 (Significance (Required)):

The work has value, since it provides a framework to address the evolutionary aspects of stem cell dynamics in flatworms. However, as the authors point multiple times, there are many unknown biological parameters, such as, for example, the ratio of cell to organism regeneration (g), and simplifications, which can significantly influence the results. For this reason, the authors provide a range of estimates for somatic mutation rates and the effective stem cell population size, rather than some final conclusions. As the authors point out, further work will be needed to refine the model but generating new data for that is beyond the scope of this manuscript. As such, I find this manuscript is an important initial contribution to the field of stem cell population dynamics in flatworms, and its methods, results and conclusions convincing. I don't have further suggestions for improving this manuscript.

Thank you very much for your positive assessment of our work.

**Referees cross-commenting**

I agree with the suggestion of Reviewer #2 that repeating the analysis on additional contings, instead of focusing only on one longest contig in the assembly, will be useful.

We will process and analyze a few additional contigs to evaluate genomic variation in transmission of somatic variants in this system.

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

**Summary:**

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

The authors aimed to use population genetics to determine the number of stem cells active in each cycle of regeneration or the equality of their relative contributions in planarians. They approached this by establishing a population with serial fission from one wild isolate of Girardia cf. tigrina collected in Italy. They used next generation sequencing to sample variants of regenerated worms at different generations of fissioning. They estimated the effective population size of stem cells to be a few hundreds, besides calculation of nucleotide diversity and somatic mutation rate. They propose small effective number of propagating stem cells might contribute to reducing reproductive conflicts in clonal organisms.

**Major comments:**

• Are the key conclusions convincing?

The mutation rate is reasonable. The effective stem cell population size and the genetic diversity may vary between different species. A small effective stem cell population size is not counter intuitive.

Generally, the work is interesting and deserves to be published.

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

The current analysis is based on many assumptions, one single set of experiments and a genome that is not well assembled. The authors have been careful with their language and documented the limitations in discussion.

• Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

I will feel more comfortable if the authors can repeat the analysis with two more random long contigs to have a better idea if the localization of markers impacts the conclusion. The concern is if different parts of the genome behave differently and if the Girardia genome is highly repetitive. As the pipeline of analysis is established, I expect this can be completed in a month with no experimental cost.

We will process and analyze a few additional contigs to evaluate genomic variation in transmission of somatic variants in this system.

• Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

Yes

• Are the data and the methods presented in such a way that they can be reproduced?

Yes

• Are the experiments adequately replicated and statistical analysis adequate?

Yes

**Minor comments:**

• Specific experimental issues that are easily addressable.

Yes.

• Are prior studies referenced appropriately?

Yes.

• Are the text and figures clear and accurate?

Yes.

• Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Yes. Please also see the significance section.

Specifically, my concerns are about writing and the context of current study.

"Small effective number of propagating stem cells might contribute to reducing reproductive conflicts in clonal organisms." is confusing. Not a good abstract ending sentence for the work presented. Reproductive conflicts need clarification. How the work relates to that concept needs support. I recommend keeping the interpretations simple and focused on the data.

Please see response under “Significance”.

Reviewer #2 (Significance (Required)):

Both questions the authors attempt to address, the genetic diversity of clonal animals and the number of stem cells contributing to regeneration, are interesting and important. The combination of these two is a bit odd in the manuscript. In other words, the population genetics approach did not address the cell biology question:how many or what proportion of stem cells are active in each cycle of regeneration. I would recommend the authors to focus the writing on one question only: the genetic diversity and evolution of a clonal species, which is driven by stem cell genome evolution and the process of regeneration. The cell biology question, phrased by the author in the abstract and introduction, need to be resolved by cell biologists. I understand the appeal to put the current study in the context of regeneration research. A balance should be achieved. Currently, the second sentence of the abstract and the first paragraph of introduction are odd and misleading. The first paragraph of the introduction can be a second paragraph to introduce the planarian system for the study.

We will restructure the manuscript to clearly separate the findings that arose directly from experimental (sequencing) data i.e. magnitude and inheritance pattern of somatic variation, and the findings that were inferred from our approximate population genetic model and depend on the unknown parameter g i.e. the effective number of stem cells and the somatic mutation rate. We will emphasize the distinction. The statements that are tangentially relevant and are not directly supported by our analyses will be modified or removed.

In the context of genetic diversity of clonal species, many studies shall be referenced. It is interesting as well to draw comparisons with other species. Asexual planarians are unique and interesting in that space.

Thus said, the attempt to examine stem cell population genetics is especially interesting and important as the fissiparous planarians do not undergo bottleneck selection by zygotes. In the context of recent progress studying planarian genetic diversity (Nishimura, O. et al. 2015, Guo, L. et al. 2016), Asgharian H. et al.'s work is timely and an important contribution to planarian researchers and evolutionary biologists. The question has general interest to cancer biologists as well. The manuscript does not have the data and is not written in a way to reach such broader audiences yet. A community is growing to address these questions.

We agree with the reviewer’s point about the pioneering works of Nishimura et al. 2015 and Guo et al. 2016. Both papers were indeed cited in our manuscript. We will cite more studies pertaining to the question of somatic genetic diversity in planarians.

The study of planarian genetic diversity has just started with two publications (Nishimura, O. et al. 2015, Guo, L. et al. 2016). It is reasonable to have lots of limitations and assumptions in the manuscript. The work is an interesting piece to be published, assuming the major points listed in the review is addressed. The reported findings will be part of the early literature and inspiration for planarian researchers and evolutionary biologists. I expect many more future manuscripts will be published, either to reexamine the reported findings or to push our understanding of the question deeper.

Thank you very much for this assessment. We fully agree.

My expertise is with planarian biology, genome, genetics, and diversity. I do not have sufficient expertise to evaluate the equations used in the study.

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Referee #2

Evidence, reproducibility and clarity

Summary:

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

The authors aimed to use population genetics to determine the number of stem cells active in each cycle of regeneration or the equality of their relative contributions in planarians. They approached this by establishing a population with serial fission from one wild isolate of Girardia cf. tigrina collected in Italy. They used next generation sequencing to sample variants of regenerated worms at different generations of fissioning. They estimated the effective population size of stem cells to be a few hundreds, besides calculation of nucleotide diversity and somatic mutation rate. They propose small effective number of propagating stem cells might contribute to reducing reproductive conflicts in clonal organisms.

Major comments:

• Are the key conclusions convincing?

The mutation rate is reasonable. The effective stem cell population size and the genetic diversity may vary between different species. A small effective stem cell population size is not counter intuitive.

Generally, the work is interesting and deserves to be published.

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

The current analysis is based on many assumptions, one single set of experiments and a genome that is not well assembled. The authors have been careful with their language and documented the limitations in discussion.

• Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

I will feel more comfortable if the authors can repeat the analysis with two more random long contigs to have a better idea if the localization of markers impacts the conclusion. The concern is if different parts of the genome behave differently and if the Girardia genome is highly repetitive. As the pipeline of analysis is established, I expect this can be completed in a month with no experimental cost.

• Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

Yes

• Are the data and the methods presented in such a way that they can be reproduced?

Yes

• Are the experiments adequately replicated and statistical analysis adequate?

Yes

Minor comments:

• Specific experimental issues that are easily addressable.

Yes.

• Are prior studies referenced appropriately?

Yes.

• Are the text and figures clear and accurate?

Yes.

• Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Yes. Please also see the significance section. Specifically, my concerns are about writing and the context of current study.

"Small effective number of propagating stem cells might contribute to reducing reproductive conflicts in clonal organisms." is confusing. Not a good abstract ending sentence for the work presented. Reproductive conflicts need clarification. How the work relates to that concept needs support. I recommend keeping the interpretations simple and focused on the data.

Significance

Both questions the authors attempt to address, the genetic diversity of clonal animals and the number of stem cells contributing to regeneration, are interesting and important. The combination of these two is a bit odd in the manuscript. In other words, the population genetics approach did not address the cell biology question:how many or what proportion of stem cells are active in each cycle of regeneration. I would recommend the authors to focus the writing on one question only: the genetic diversity and evolution of a clonal species, which is driven by stem cell genome evolution and the process of regeneration. The cell biology question, phrased by the author in the abstract and introduction, need to be resolved by cell biologists. I understand the appeal to put the current study in the context of regeneration research. A balance should be achieved. Currently, the second sentence of the abstract and the first paragraph of introduction are odd and misleading. The first paragraph of the introduction can be a second paragraph to introduce the planarian system for the study.

In the context of genetic diversity of clonal species, many studies shall be referenced. It is interesting as well to draw comparisons with other species. Asexual planarians are unique and interesting in that space.

Thus said, the attempt to examine stem cell population genetics is especially interesting and important as the fissiparous planarians do not undergo bottleneck selection by zygotes. In the context of recent progress studying planarian genetic diversity (Nishimura, O. et al. 2015, Guo, L. et al. 2016), Asgharian H. et al.'s work is timely and an important contribution to planarian researchers and evolutionary biologists. The question has general interest to cancer biologists as well. The manuscript does not have the data and is not written in a way to reach such broader audiences yet. A community is growing to address these questions.

The study of planarian genetic diversity has just started with two publications (Nishimura, O. et al. 2015, Guo, L. et al. 2016). It is reasonable to have lots of limitations and assumptions in the manuscript. The work is an interesting piece to be published, assuming the major points listed in the review is addressed. The reported findings will be part of the early literature and inspiration for planarian researchers and evolutionary biologists. I expect many more future manuscripts will be published, either to reexamine the reported findings or to push our understanding of the question deeper.

My expertise is with planarian biology, genome, genetics, and diversity. I do not have sufficient expertise to evaluate the equations used in the study.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Many flatworm species reproduce asexually, by fission, and the process relies on the activity of stem cells (neoblast), which drive regeneration. The question that this work tries to address is what is the dynamics of stem cells in this process, including how many stem cells contribute to regeneration, what are the mutation rates and selection mechanisms, if any. Towards this, the authors tracked one specimen of planarian Girardia tigrina for more than ten rounds of fission, and re-sequenced its genome at multiple time points and applied methods of population genetics to analyze and model the data. The main conclusion of the work is that there is high somatic mutation rate, rapid loss of heterozygosity, and a small size of the stem cell population that contributes to regeneration after fission.

Significance

The work has value, since it provides a framework to address the evolutionary aspects of stem cell dynamics in flatworms. However, as the authors point multiple times, there are many unknown biological parameters, such as, for example, the ratio of cell to organism regeneration (g), and simplifications, which can significantly influence the results. For this reason, the authors provide a range of estimates for somatic mutation rates and the effective stem cell population size, rather than some final conclusions. As the authors point out, further work will be needed to refine the model but generating new data for that is beyond the scope of this manuscript. As such, I find this manuscript is an important initial contribution to the field of stem cell population dynamics in flatworms, and its methods, results and conclusions convincing. I don't have further suggestions for improving this manuscript.

Referees cross-commenting

I agree with the suggestion of Reviewer #2 that repeating the analysis on additional contings, instead of focusing only on one longest contig in the assembly, will be useful.

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Reply to the reviewers

We want to thank the reviewers for their careful evaluation of our work and their helpful suggestions. We provide at the end of this letter a point by point response of how we aim to address their concerns, which can be summarised in the following main points:

1-We will provide further evidence for the efficiency and dynamics of beta-catenin deletion in adult neural stem cells in vivo (point raised by both reviewers).

We fully agree that although we tested for the disappearance of beta-catenin transcripts in sorted NSCs after deletion, providing further proof of the absence of beta-catenin protein in these cells will help strengthen our conclusions. For this, we are performing additional stainings for beta-catenin and Wnt/beta-catenin targets, together with neural stem cell markers, to quantify the loss of beta-catenin and Wnt/beta-catenin signalling in NSCs at P90 (30 days after deletion), as well as new P150 samples (90 days after deletion).

2-We will investigate in further detail the effects (or lack of effect) of beta-catenin deletion on adult neurogenesis.

The focus of our work is the effect of Wnt/beta-catenin signalling on NSCs. Nevertheless, we agree with reviewer 2 that extending our analysis to later stages in the neurogenic process will be of importance to better contrast our results with previous reports identifying a role for Wnt in neuronal production in the adult hippocampus. We are currently processing new material from mice in which beta-catenin was deleted at P60 and brains collected after 3 months to evaluate the long-term effects of beta-catenin deletion on the neurogenic output of NSCs. We will also perform stainings of Wnt-responsive neuronal genes, such as NeuroD1 and Prox1, at P90 and P150 in both control and beta-catenin cKO mice.

3- We are aiming to confirm that the in vitro effects of CHIR99021 on NSCs are mediated by beta-catenin. We already provide evidence that stimulation with Wnt3a has the same effect as inhibition of GSK3beta by CHIR99021. To further prove the link of the observed effects to Wnt-beta-catenin signalling, we will repeat some of our key experiments using beta-catenin floxed cells (both induction of neuronal differentiation and re-activation from quiescence) as reviewer 1 suggests.

Reviewer #1

Overall, the results are reliable and important for the field. However, several points need to be addressed and clarified to support their conclusion. I am hopeful that the authors find my comments helpful and constructive.

Many thanks for your insightful comments, we believe they will indeed help us improve our manuscript.

1. • Validation of cKO in vivo.*

• Although the authors validated cKO of beta-catenin in vivo using FACS/qPCR at the transcript level, it would be important to check when and to what extent beta-catenin proteins are downregulated in qNSC/activeNSCs in vivo. This will be easily assessed by immunohistochemistry. In the same line, although the authors confirmed the reduction of beta-catenin signaling using beta-gal signaling in cKO mice, it would be important to check if this can be cross-checked by staining the nuclear localization of beta-catenin. This confirmation would strength the authors statement and clear that some remained beta-catenin at the plasma membrane may not be compensating their function.*

• Independent of the confirmation of beta-catenin cKO, it would be important to check if the downstream targets of Wnt/beta-catenin signals (ex. Expression of Axin2) were also attenuated. This point should be addressed both in vivo and in vitro. *

We are performing immunohistochemistry and quantification of beta-catenin in control and cKO brain samples, as suggested by the reviewer. Unfortunately, we have not yet found an antibody and labelling protocol that allows us to detect nuclear beta-catenin, even in control samples, so with our current antibody, we won’t be able to show a reduction in nuclear localization of beta-catenin in the cKO samples. We are testing alternative beta-catenin antibodies that could help us overcome this limitation. As the reviewer mentions, we do see a reduction in reporter expression in BATGAL mice upon deletion of beta-catenin. In order to further demonstrate effective Wnt signalling attenuation in our mutant mice we are testing antibodies for Wnt targets such as Axin2, CcnD1 and NeuroD1.

• Wnt/beta-catenin signals in qNSC and active NSC in vitro.*

The authors indicated that the depletion of beta-catenin had no effect on qNSCs and active NSCs in vitro. However, it is not clear whether Wnt/beta-catenin signaling is activated in their culture conditions. If there are no inputs of Wnt signaling in cultured cells, the depletion of beta-catenin will not lead any impacts. Therefore, it would be critical to check if the Wnt-signaling is activated in control cells in their culture condition, and if the downstream targets of Wnt-signaling are downregulated in cKO qNSCs/active NSCs.

We agree that this is an important conceptual point that needs to be clarified. From our data (see Figure S3C), we can see that deletion of beta-catenin in NSCs in vitro blocks their response to Wnt stimulation (with CHIR99021) but it did not lower the levels of Axin2. From this, we can deduce that Wnt signalling is indeed not significantly activated in proliferating NSCs in vitro, despite the expression of Wnt ligands by these cells (Figure 3). We will perform further analysis of Wnt target genes in control and cKO NSCs in vitro to confirm this observation. Of note, the lack of Wnt signalling activity in NSCs would further support our claim that Wnt is dispensable for their proliferation and maintenance. We will make this point clearer in the manuscript.

• ChIR treatment on cKO cells.*

The authors only use WT cells for ChIR treatment. To investigate whether the effect of ChIR come through the beta-catenin signaling pathway, why don't they use cKO NSCs for ChIR treatment (Fig5-7)?

This is a great suggestion and we are performing these experiments with control and cKO NSCs.

Different Wnt signaling levels between in vivo and in vitro.

The authors indicated that different levels of Wnt signaling could results in different outcomes based on in vitro observation. What are the levels of Wnt signaling in vivo compared to in vitro ChIR treatment? Activation of Wnt/beta-catenin in vivo is much weaker than in vitro CHIR treatment, therefore the contribution of Wnt signaling at endogenous levels is negligible? This may help to explain why Wnt/beta-catenin is dispensable in vivo, at least in young state. This can be addressed by probing the levels of downstream targets.

Levels of Wnt signalling are indeed central to our conclusions and we agree that a comparison of Wnt/beta-catenin signalling levels between our in vitro interventions and the in vivo situation would be important. However, we find that directly comparing the levels of downstream Wnt targets between the two systems might prove challenging due to differences in methodology (immunolabeling is not a reliably quantitative method, especially when performed on such different sample types, with different fixation conditions, etc). We will nevertheless attempt such quantifications using immunolabelings for CcnD1, Axin2 and NeuroD1 both in vivo and in vitro. We also want to point out that CHIR is not the only way in which we have stimulated Wnt signalling in NSCs in vitro. In Figure S5, we demonstrate that treatment with Wnt3a can reactivate quiescent neural stem cell in a dose-dependent manner, showing that the effect of Wnt signalling on NSCs can be achieved also with a more physiological intervention.

Reviewer #2

A major challenge is to separate cell adhesion functions of beta-catenin from its function in the canonical Wnt/beta-catenin signaling pathway. The authors tested two different conditional bcat alleles (bcatdel ex2-6 ; bcatdel ex3-6) to delete bcat from stem cells. It is a bit unfortunate that the authors chose to test two conditional alleles that would affect cell adhesion and transcriptional activity instead of the Ctnnb1dm allele (Draganova et al. 2015, Stem Cells), which would have been a cleaner way to specifically address the contribution of beta-catenin transcriptional activity in adult hippocampal neural stem cells. Was there a specific reason not to use the Ctnnb1dm conditional mice? Please comment / discuss.

We agree with the reviewer that the Ctnnb1dm allele would better differentiate between cell adhesion and transcriptional effects of beta-catenin deletion. However, as we see no effect of beta-catenin deletion, we did not find it necessary to further dissect the differential contribution of cell adhesion and the Wnt/beta-catenin pathway in this particular case. We will add a comment on this point to the discussion.

The authors control for downregulation of beta-catenin signaling activity in the bcatdel ex2-6 through the analysis of the BATGAL reporter. 30 days after recombination, they observe a drop in reporter activity (from 31% to 13%). While this drop shows that at the time of analysis beta-catenin signaling activity was reduced, the lack of complete downregulation of reporter activity raises the issue whether long-term stability of the b-catenin protein may be a confounding factor at this time-point. In particular effects of b-catenin on the DCX population, which to a significant extent is generated several days to weeks before the time-point of analysis, may not be revealed. Data on the time-course of downregulation of the BATGAL reporter could help for the interpretation of the data as would analysis of beta-catenin protein levels in recombined cells. In addition, analysis of bcatdel ex2-6 at a later time-point after recombination, at which beta-catenin signaling activity is further downregulated, would strengthen the surprising finding that loss of beta-catenin signaling activity does not hamper neuronal differentiation in the adult hippocampus.

We will monitor the disappearance of beta-catenin using immunohistochemistry for beta-catenin and downstream targets of Wnt in control and cKO brains, both at P90 and at a longer time after deletion (P150), as the reviewer suggests. Of note, when we deleted beta-catenin in vitro in NSCs, we could confirm the disappearance of the protein by 48 hours, and therefore beta-catenin stability cannot explain the lack of effect of the deletion (Figure S3B).

Was quantification performed only in recombined (i.e., reporter positive) cells or in recombined and non-recombined cells? I could not locate that information. Given the evidence for feed-back regulation from intermediate precursor cells / immature neurons to stem cells (e.g. Lavado et al. 2010, Plos Biology), it is important to separately evaluate the development of recombined and non-recombined cells to evaluate the behavior of beta-catenin signaling deficient stem cells.

The quantifications were always performed in YFP+ recombined cells. The efficiency of recombination was very high (from 83 to 97%), therefore allowing no room for confounding effects of unrecombined cells. We will convey this information in a clearer way in our revised manuscript.

Reports from (Kuwabara et al. 2009, Nat Neurosci), (Gao et al. 2009, Nat Neurosci) and (Karalay et al. 2011, PNAS) suggest that beta-catenin signaling activity drives dentate granule neuron identity through regulating the expression of Neurod1 and Prox1. Given that in these studies neither loss of Neurod1 nor of Prox1 affects neuronal fate commitment but long-term survival and that the studies by (Gao et al. 2007, J Neurosci) and (Heppt et al. 2020, EMBO J) suggest that loss-of-beta-catenin affects neuronal survival, it may be interesting to evaluate a) whether a dentate granule neuron identity, b) long-term survival of adult generated neurons are affected. At the minimum these studies should be more extensively discussed.

As mentioned in our response summary, our main aim is to test the effects of Wnt/beta-catenin signalling on NSCs. Nevertheless, these are excellent suggestions and we are currently performing immunohistochemistry for NeuroD1 and Prox1 to test whether they are downregulated in cKO brain samples. We have also performed a longer deletion of beta-catenin (deletion at P60 and analysis at P150) to test whether neurogenesis is affected in the cKO mice in the longer term.

It has been suggested that the neural stem cell population in the adult hippocampus may be heterogenous with one population being responsible for baseline neurogenesis and being resistant to age-associated depletion and a second population driving high levels of neurogenesis in young adults (see also Urban, Bloomfield and Guillemot 2019, Neuron). The observation that beta-catenin signaling is only active in a small fraction of stem cells and their progeny raises the question whether it fulfills only a function in a specific subpopulation. Such possibility should at least be discussed.

This is a very interesting point, which we will include in the discussion of our revised manuscript. We are also performing immunohistochemistry for Id4 together with beta-catenin or downstream targets of Wnt and NSC markers to determine whether the resting population (described in Urban et al. 2016 and Harris et al. 2021), which has low levels of Id4 is more responsive to Wnt than the dormant population.

The recently published studies by (Rosenbloom et al. 2020, PNAS) and (Heppt et al. 2020, EMBO J) strongly suggest that beta-catenin signaling dynamics are critical for the regulation / modulation of adult hippocampal neurogenesis. The aspect of beta-catenin signaling dynamics should be discussed.

We will include a discussion of beta-catenin signalling dynamics in the revised version of the manuscript.

**Significance:**

Adult neurogenesis is considered an important factor in hippocampal plasticity and its disturbance is thought to contribute to the pathogenesis in several psychiatric and degenerative diseases. Wnt/beta-catenin signaling is considered central to the regulation of adult hippocampal neurogenesis. In this regard, the manuscript describes the potentially very important and surprising finding that deletion of beta-catenin from neural stem cells does not generate major neurogenesis phenotypes. The concern with the present manuscript is, that the lack of phenotype requires additional analyses to exclude that phenotypes develop with a delay because of long-term stability of the beta-catenin protein.

We believe the revisions outlined above will address these concerns.

The significance of the manuscript and its interest to a wider audience would in addition be greatly enhanced, if the authors could provide some mechanistic data that would explain the discrepancies between published functions of Wnt/beta-catenin-signaling dependent regulation of neurogenesis and their own findings. The manuscript would also gain significance if the authors would provide solid data for their interesting hypothesis that beta-catenin-signaling contributes to the regulation of adult hippocampal neurogenesis in response to extrinsic stimuli. In this regard one potential approach would be to analyse whether extrinsic stimuli such as running would be able stimulate the activation of stem cells.

Both finding a mechanism to explain the observed discrepancies and demonstrating that Wnt has a role in the response of NSCs to extrinsic stimuli are excellent follow-up suggestions to our work and we thank the reviewer for these recommendations. However, addressing these points would take many months (if not years) and is not necessary to support the current conclusions of our work. We therefore believe they are out of the scope of this current manuscript.

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Referee #2

Evidence, reproducibility and clarity

Summary:

Wnt/beta-catenin signaling is considered central to the regulation of adult hippocampal neurogenesis. In this manuscript Austin and colleagues interrogate the function of beta-catenin-dependent signaling using in vivo beta-catenin conditional knockout and gain-of-function approaches combined with in vitro pharmacological and genetic approaches. The authors confirm previous reports of Wnt/beta-catenin signaling in adult hippocampal neurogenesis and report the surprising findings that • Deletion of beta-catenin from stem cells does not affect stem cell numbers and their activation / proliferation in vivo and in vitro • Deletion of beta-catenin from stem cells does not affect neuronal differentiation in vivo and in vitro Moreover, the authors show that expression of a stabilized form of beta-catenin affects stem cell positioning in vivo and that the effects of treatment of cultured hippocampal stem/progenitor cells with a pharmacological stimulator of Wnt/beta-catenin signaling are dose and time-dependent. The authors discuss that their findings suggest that Wnt/beta-catenin signaling is dispensable for neural stem cell homeostasis and that Wnt/beta-catenin signaling may have a function in the response of stem cells to external stimuli.

Comments:

A major challenge is to separate cell adhesion functions of beta-catenin from its function in the canonical Wnt/beta-catenin signaling pathway. The authors tested two different conditional bcat alleles (bcatdel ex2-6 ; bcatdel ex3-6) to delete bcat from stem cells. It is a bit unfortunate that the authors chose to test two conditional alleles that would affect cell adhesion and transcriptional activity instead of the Ctnnb1dm allele (Draganova et al. 2015, Stem Cells), which would have been a cleaner way to specifically address the contribution of beta-catenin transcriptional activity in adult hippocampal neural stem cells. Was there a specific reason not to use the Ctnnb1dm conditional mice? Please comment / discuss.

The authors control for downregulation of beta-catenin signaling activity in the bcatdel ex2-6 through the analysis of the BATGAL reporter. 30 days after recombination, they observe a drop in reporter activity (from 31% to 13%). While this drop shows that at the time of analysis beta-catenin signaling activity was reduced, the lack of complete downregulation of reporter activity raises the issue whether long-term stability of the b-catenin protein may be a confounding factor at this time-point. In particular effects of b-catenin on the DCX population, which to a significant extent is generated several days to weeks before the time-point of analysis, may not be revealed. Data on the time-course of downregulation of the BATGAL reporter could help for the interpretation of the data as would analysis of beta-catenin protein levels in recombined cells. In addition, analysis of bcatdel ex2-6 at a later time-point after recombination, at which beta-catenin signaling activity is further downregulated, would strengthen the surprising finding that loss of beta-catenin signaling activity does not hamper neuronal differentiation in the adult hippocampus.

Was quantification performed only in recombined (i.e., reporter positive) cells or in recombined and non-recombined cells? I could not locate that information. Given the evidence for feed-back regulation from intermediate precursor cells / immature neurons to stem cells (e.g. Lavado et al. 2010, Plos Biology), it is important to separately evaluate the development of recombined and non-recombined cells to evaluate the behavior of beta-catenin signaling deficient stem cells.

Reports from (Kuwabara et al. 2009, Nat Neurosci), (Gao et al. 2009, Nat Neurosci) and (Karalay et al. 2011, PNAS) suggest that beta-catenin signaling activity drives dentate granule neuron identity through regulating the expression of Neurod1 and Prox1. Given that in these studies neither loss of Neurod1 nor of Prox1 affects neuronal fate commitment but long-term survival and that the studies by (Gao et al. 2007, J Neurosci) and (Heppt et al. 2020, EMBO J) suggest that loss-of-beta-catenin affects neuronal survival, it may be interesting to evaluate a) whether a dentate granule neuron identity, b) long-term survival of adult generated neurons are affected. At the minimum these studies should be more extensively discussed.

It has been suggested that the neural stem cell population in the adult hippocampus may be heterogenous with one population being responsible for baseline neurogenesis and being resistant to age-associated depletion and a second population driving high levels of neurogenesis in young adults (see also Urban, Bloomfield and Guillemot 2019, Neuron). The observation that beta-catenin signaling is only active in a small fraction of stem cells and their progeny raises the question whether it fulfills only a function in a specific subpopulation. Such possibility should at least be discussed.

The recently published studies by (Rosenbloom et al. 2020, PNAS) and (Heppt et al. 2020, EMBO J) strongly suggest that beta-catenin signaling dynamics are critical for the regulation / modulation of adult hippocampal neurogenesis. The aspect of beta-catenin signaling dynamics should be discussed.

Significance

Significance:

Adult neurogenesis is considered an important factor in hippocampal plasticity and its disturbance is thought to contribute to the pathogenesis in several psychiatric and degenerative diseases. Wnt/beta-catenin signaling is considered central to the regulation of adult hippocampal neurogenesis. In this regard, the manuscript describes the potentially very important and surprising finding that deletion of beta-catenin from neural stem cells does not generate major neurogenesis phenotypes. The concern with the present manuscript is, that the lack of phenotype requires additional analyses to exclude that phenotypes develop with a delay because of long-term stability of the beta-catenin protein.

The significance of the manuscript and its interest to a wider audience would in addition be greatly enhanced, if the authors could provide some mechanistic data that would explain the discrepancies between published functions of Wnt/beta-catenin-signaling dependent regulation of neurogenesis and their own findings. The manuscript would also gain significance if the authors would provide solid data for their interesting hypothesis that beta-catenin-signaling contributes to the regulation of adult hippocampal neurogenesis in response to extrinsic stimuli. In this regard one potential approach would be to analyse whether extrinsic stimuli such as running would be able stimulate the activation of stem cells.

Expertise:

Adult neurogenesis, stem cell biology, signaling

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Referee #1

Evidence, reproducibility and clarity

Summary

Wnt/beta-catenin signaling has been studies in the context of adult neurogenesis for decades. It has been shown that modulation of Wnt signaling regulates adult neurogenesis, but the consequences were not always consistent. In this study, the authors developed conditional knockout mouse lines to test whether beta-catenin is essential for the regulation of adult neurogenesis.

First, using a published single cell seq-data and a reporter TG mouse system, they validated the expression of Wnt-pathway molecules in qNSCs and active NSCs. Then, beta-catenin conditional cKO mice were analyzed. The authors did not find any changes in total number of NSCs, the activation of NSCs, and the number of IPCs as well as neuroblasts. Subsequently, using in vitro culture system, the authors addressed if the proliferation and differentiation are affected in vitro conditions. Both proliferation and activation from the quiescent state were not affected in cKO NSCs. Finally, they demonstrated that an artificial stimulation of Wnt signaling by CHIR can induce differentiation or proliferation depending on cellular states and doses, thus NSCs can respond to Wnt signaling. Based on these data, they concluded that beta-catenin is dispensable for the maintenance/activation of NSCs in vivo, although NSCs can respond to Wnt/beta-catenin signaling. Overall, the results are reliable and important for the field. However, several points need to be addressed and clarified to support their conclusion. I am hopeful that the authors find my comments helpful and constructive.

1. Validation of cKO in vivo. Although the authors validated cKO of beta-catenin in vivo using FACS/qPCR at the transcript level, it would be important to check when and to what extent beta-catenin proteins are downregulated in qNSC/activeNSCs in vivo. This will be easily assessed by immunohistochemistry. In the same line, although the authors confirmed the reduction of beta-catenin signaling using beta-gal signaling in cKO mice, it would be important to check if this can be cross-checked by staining the nuclear localization of beta-catenin. This confirmation would strength the authors statement and clear that some remained beta-catenin at the plasma membrane may not be compensating their function. Independent of the confirmation of beta-catenin cKO, it would be important to check if the downstream targets of Wnt/beta-catenin signals (ex. Expression of Axin2) were also attenuated. This point should be addressed both in vivo and in vitro.
2. Wnt/beta-catenin signals in qNSC and active NSC in vitro The authors indicated that the depletion of beta-catenin had no effect on qNSCs and active NSCs in vitro. However, it is not clear whether Wnt/beta-catenin signaling is activated in their culture conditions. If there are no inputs of Wnt signaling in cultured cells, the depletion of beta-catenin will not lead any impacts. Therefore, it would be critical to check if the Wnt-signaling is activated in control cells in their culture condition, and if the downstream targets of Wnt-signaling are downregulated in cKO qNSCs/active NSCs.
3. ChIR treatment on cKO cells The authors only use WT cells for ChIR treatment. To investigate whether the effect of ChIR come through the beta-catenin signaling pathway, why don't they use cKO NSCs for ChIR treatment (Fig5-7)?
4. Different Wnt signaling levels between in vivo and in vitro<br> The authors indicated that different levels of Wnt signaling could results in different outcomes based on in vitro observation. What are the levels of Wnt signaling in vivo compared to in vitro ChIR treatment? Activation of Wnt/beta-catenin in vivo is much weaker than in vitro CHIR treatment, therefore the contribution of Wnt signaling at endogenous levels is negligible? This may help to explain why Wnt/beta-catenin is dispensable in vivo, at least in young state. This can be addressed by probing the levels of downstream targets.

Significance

Significant.

A genetic approach to address the role of Wnt/Beta-catenin signaling is critical for the field. The audience would be interested if this study make it clear previously reported discrepancy.

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Reply to the reviewers

Response to reviewers

We first thank Review Commons for recruiting such knowledgeable reviewers to comment on our manuscript. We appreciate their diverse set of useful and constructive comments, which should help us improve the manuscript substantially. Please see our response to each reviewer’s comments below.

Reviewer #1:

**Summary:** The authors describe a useful modified fluctuation assay that couples conventional mutation rate analysis with mutational spectrum characterization of forward mutations at the S. cerevisiae CAN1 locus. They nicely showed that wild yeast isolates display a wide range of mutation rates with strains AAR and AEQ displaying rates ~10-fold higher than the control lab strain. These two strains also showed a bias for C>A mutations, and were the only strains analyzed that had a mutation spectrum statistically different from the lab control. Together, these data provide a compelling proof-of-principle of the applicability of the modified fluctuation analysis approach described in this manuscript. Overall, the manuscript is very well written, and the work reported in it does represent a valuable contribution to the field. However, two primary shortcomings were identified that can be addressed to strengthen the conclusions prior to publication. Both points described below pertain to the analysis of the possible C>A specific mutator phenotype in strains AAR and AEQ.

Response:

We thank the reviewer for this positive response. We have made a plan, detailed below, to address the shortcomings the reviewer has highlighted.

**Major comments:**

1. The work presented in the manuscript does suggest that these two haploids are likely to display the C>A mutator phenotype. Yet, the authors fell short of providing a full and unambiguous demonstration that would elevate the significance of their discovery. They could have directly tested the predicted C>A specific mutator phenotype by conducting additional experiments, one of which is relatively simple. Specifically, they could have performed a simple reversion-based mutation assay to validate the reported C>A mutator phenotype displayed by AAR and AEQ. For example, into AAR, AEQ, and a wild type control, the authors could introduce an engineered auxotrophic marker allele (e.g., ura3 mutation) caused by an A to C substitution, which upon mutation back to A restores prototrophic growth in minimal media (ie. reversion from ura3-C to URA3-A). Such specific reversible allele should be relatively easy to integrate into the AAR and AEQ genomes, as well as in the control strain. Based on the authors' prediction, AAR and AEQ should display a very large increase (far higher than 10 fold) in the reversion rate when compared to a control haploid. To demonstrate the specificity of the mutation spectrum, the authors could test the reversion rates of a different engineered allele requiring a reversion mutation in the opposite direction (ie. reversion from ura3-A to URA3-C). If the AAR and AEQ mutator is specific C>A, one would predict that all three strains should have similar mutation rates for a reversion in the A>C direction. This additional genetic work would thoroughly validate the central discovery and would reinforce the usefulness of the method described in the manuscript.

Alternatively, a conventional mutation accumulation and whole genome re-sequencing experiment with parallel lines of AAR, AEQ and a control strain would also very effectively validate the C>A mutator prediction, and it would also answer the authors' discussion point about specificity to the CAN1 locus. However, it would be more costly and much more time consuming.

Response:

We thank the reviewer for these detailed, clear suggestions regarding additional methodology for further validating our results. We appreciate that parallel independent validations always add credibility to unexpected results like the ones presented in our manuscript. We’ve been considering these suggestions seriously, but our concern is that it is much less straightforward to engineer the genomes of these wild yeast than one might expect based on experiments with standard laboratory strains. Unforeseen roadblocks related to the biology of AAR and AEQ could end up making the URA3 reversion assay take even longer than an MA study. As we understand it, the two main concerns that might necessitate this additional undertaking are that either our novel assay for ascertaining mutations in CAN1 doesn’t work properly, or that the mosaic beer strains mutate significantly differently outside CAN1. Below we describe revisions to the text that we think will clearly represent these caveats and the relatively modest uncertainty associated with them.

To further justify the soundness of our claim that AAR and AEQ have distinctive mutation rates and spectra, we plan to add additional discussion of the validation approaches that are presented in the manuscript to verify the accuracy of our pipeline. Although the ability of fluctuation assays to estimate mutation rates is well established, the identification of the spectra using our next-generation-sequencing-based pipeline is novel, so we used Sanger sequencing to validate the exact de novo mutations it ascertained in a select control strain. Our Sanger sequencing test found our assay to have an undetectably low false positive rate and a false negative rate that was much too low to account for the differences we measured between AAR, AEQ, and the standard lab strains. The fact that we also observed similar mutation spectra from control lab strains used in previous CAN1-based studies further demonstrates the reliability of our method, and it is notable that most natural isolates were measured to have very similar mutation spectra to lab strains (Figure 4 and Supplementary Figure S8-S9). We agree that further validation would be needed to read much into the more subtle differences in mutation rates and spectra that we saw hints of between other strains, and for that reason, we focused this paper on the differences that well exceed what we measured to be our measurement pipeline’s margin of error.

It is true that the genome-wide mutation rate might differ somewhat from the mutation rate at the CAN1-locus, but the mutation spectrum at the CAN1 locus measured in a previous study (Lang and Murray, 2008) was very similar to the genome-wide mutation spectra obtained from MA studies (Sharp et al., 2018), with just a small overall increase of mutations with C/G nucleotides (the second to last paragraph on page 17 and Supplementary Figure S13). Moreover, we have avoided making any claims of seeing distinct mutation rates or spectra based on “apples-to-oranges” comparisons between mutation spectra measured at CAN1 and spectra measured across the whole genome.

We also note that the enrichment of C>A mutations in AEQ and AAR is not only observed from our de novo mutation data in CAN1, but also seen in rare natural polymorphisms genome-wide (Figure 1B, 5A,B). Rare natural polymorphisms are recent mutations that occurred during the history of the strain, and the fact that they disproportionately enrich in C>A mutations in these strains indirectly shows that the C>A enrichment occurs not only at CAN1, as measured in our experiment, but has also been occurring during natural mutation accumulation genome-wide.

The second concern is in regard to the relatively extensive conclusions drawn about the possible evolutionary significance of the possible C>A mutator in AAR and AEQ. The authors should be more cautious and conservative in the proposed interpretation. As the authors note:

'Three of the four C>A-enriched mosaic beer strains, AAR, AEQ, and SACE_YAG, are all haploid derivatives of the [highly heterozygous] diploid Saccharomyces cerevisiae var diastaticus strain CBS1782, which was isolated in 1952 from super-attenuated beer.'

From this statement, and because the paper cited provided few details on the isolation of CBS1782, it is presumed that these haploid derivatives were most likely isolated as recombinant spores. Furthermore, it is unclear when this isolation occurred, and for how many generations strains AAR and AEQ have been propagated in a haploid state.

Herein lies a critical point: AAR and AEQ were recently derived from a diploid background with a "high level of heterozygosity". In a heterozygous diploid context, deleterious point mutations (and any resulting mutator phenotypes) would likely be masked by the presence of wild-type alleles. Now, as haploids, they express a novel genotype (i.e., combination of defective or incompatible parental alleles), which manifests as a mutator phenotype. In this respect, AAR and AEQ appear analogous to the spore derivatives of the incompatible cMLH1-kPMS1 isolate referred to in the manuscript as a notable exception. The analysis of strains harboring incompatible MLH1-PMS1 mutations by Raghavan et al. demonstrated that the heterozygous diploid parents were not themselves mutators, but that haploid spores which had inherited the pair of incompatible alleles displayed mutator phenotype. Collectively, while it can certainly be argued that the strains AAR and AEQ (like the MLH1/PMS1 incompatible strains) are mutators now, this fact alone does not support the conclusion that they have adapted to survive the expression of an extant mutator phenotype. This premise could be tested by analyzing the mutation rates/spectra of four new spores derived from a single tetrad of CBS 1782. Do the four sibling spores display similar or different mutational rates and spectra? If all four spores from a single tetrad exhibit the 10-fold increase in CAN1 mutation rate and the C>A transversion bias, then it can be inferred that the diploid parent is also a mutator in the same manner. Further direct analysis of mutation rates and spectrum in the parent diploid CBS 1782 would complete the work. This finding would be quite significant, and would provide strong evidence that wild strains can in fact tolerate the expression of a chronic mutator allele.

Response:

We thank the reviewer for suggesting additional study of the ancestral diploid strain CBS 1782, and we agree this could add a lot to the manuscript, especially given the high level of heterozygosity in the diploid and the link to the previous MLH1-PMS1 incompatibility story. We have obtained a sample of CBS 1782 and plan to knock out its HO locus using CRISPR, perform tetrad dissection of spores freshly derived from the diploid, and then measure mutation rates and spectra in all four segregants derived from a single tetrad (provided that all four spores end up growing). We plan to collect and sequence about 50 mutations to get qualitative results on the mutation rates and spectra of these segregants. We also plan to sequence the whole genome of the strain CBS 1782 and examine polymorphisms together with the 1011 strains to check for any signal of C>A enrichment. We recognize that our pipeline as currently implemented will not let us directly measure the mutation spectrum of the diploid, which is inaccessible to our pipeline given its two functional copies of CAN1 and the recessive nature of canavanine resistance. That being said, the elevation of the C>A fraction in natural polymorphisms found in AAR and AEQ provides evidence for prolonged activity of the mutator phenotype in the wild and/or in the domesticated environment from which CBS 1782 was derived. However, we acknowledge we have limited information about how these haploids were propagated before they were banked.

**Minor comments:** A final, relatively minor point. That the new haploids AAR and AEQ show distinct mutation rates and spectra opens the door to an interesting line of inquiry, which may help to identify the causative mutator allele in a manner more efficient than searching for missense mutations. It is stated, and it is understandable, that the identification of the possible causal mutations is beyond the scope of the present manuscript. In this spirit, it would be much more appropriate to restrict such considerations to the Discussion section. Specifically, while the authors make a plausible case for OGG1 being a candidate gene responsible for the C>A mutator phenotype, no experimental demonstration was attempted. As such, that text segment should be moved from the Results to the Discussion section.

Response:

We agree with the reviewer of lacking genetic evidence on OGG1 in the current manuscript and we will move that section from the results to the discussion. Future work is underway to test and identify the causal loci for the mutator phenotype.

Reviewer #1 (Significance (Required)): As stated in the summary section above, the manuscript by Jiang et al represents a substantial contribution to the fields of genome stability and genome evolution. The method described is likely to be useful beyond budding yeast. The work will be appreciated by a broad audience of geneticists. The additional work and text modifications proposed above would likely further elevate the impact of this work.

Response:

We are very grateful for this generous assessment and we likewise hope our planned revisions will further elevate the paper’s potential impact.

Reviewer #2:

Mutation is a fundamental force in organismal evolution, and therefore understanding the evolution of mutational mechanisms are important in evolutionary studies. In this manuscript, the authors used strains of S. cerevisiae as a model system to study the variations of rates and spectra in mutations with bioinformatic and experimental approaches. First, the authors analyzed the polymorphism data from 1011 strains by PCA analysis and show the variations in spectra. Second, the authors used fluctuation test combined with deep sequencing of the resistance gene to identify mutation rates and spectra in 18 strains, which show ~10-fold mutation rate variations and increased C-to-A mutations in two strains.

For the second part, the experimental procedures and statistical analysis are mostly solid. For the first part, as what authors said in the introduction, polymorphism is not equal to the mutation spectra. I think the authors did a good job by being cautious in the wording and having no over-inference after the analysis. It is thus inevitable that the conclusion of this part sounds mostly descriptive. The overall writing is very clear. I will recommend the publication in field-specific journals.

Response:

We thank the reviewer for these positive comments. We will address each minor point below.

**Minor comments:** P9 - It is very hard to not wonder how the 16 strains were picked in the fluctuation tests. Some comments on that will be appreciated. E.g., was that informed by the results of Fig 1?

Response:

We actually did not pick strains based on the results of Figure 1, one reason being that the CAN1 reporter method only works on haploid strains with a canavanine sensitivity phenotype. We also restricted our analysis to strains without known aneuploidies to maximize our ability to accurately measure the spectra of the strains’ polymorphisms. When possible, given these constraints, we included at least two randomly selected strains from each clade of the 1011 collection whenever possible. These constraints are currently explained on the second to last paragraph on page 9, and will be explained in more detail in revision.

P17- In the paragraph "natural selection might contribute ..." , is there any example of "certain mutation types are more often beneficial than others"?

Response:

One example of this is that transitions are more often synonymous than transversions are (Freeland and Hurst, 1998), and mutations that create or destroy CpG sites are more likely to alter gene regulation than other mutation types are (in species other than yeast where CpGs are methylated). We recognize that these effects are likely not large, which is one reason we don’t think natural selection is a great explanation for mutation spectrum difference among groups.We will mention these examples explicitly in the revised text.

P20 - Extra ')' in the sentence "Adjacent indels were merged if their frequencies differed by less than 10%)."

Response:

We will fix this in revision.

In the discussion, it might be good to add a paragraph to compare the rate and spectra reported here and the ones found by MA and then NGS approach(e.g., Zhu et al. 2014).

Response:

We’ll be sure to add a reference to the Zhu et al. (2014) spectrum in the discussion, extending our existing comparison of mutation spectra previously reported using CAN1 (Lang and Murray, 2008) and the MA approach (Sharp et al., 2018) (currently discussed on the second to last paragraph on page 17, Supplementary Figure S13). Our CAN1 method also obtains results that are consistent with the Lang et al 2008 study on the same control strain (the last paragraph on page 11).

Reviewer #2 (Significance (Required)): The significance of this manuscript will be relatively specific to evolutionary biologists and geneticists, especially those who use yeasts as a model system. For example, I expect the variation of mutation rates and spectra found in this manuscript will impact the following population-genetic analysis in this collection of 1011 strains and motivate more studies on the molecular machineries which affect mutation rates and spectra.

In addition, in terms of methodological novelty, adding a novel step of reporter-gene sequencing is a reasonable way to get some information on mutation spectra as it is less labor-intensive than NGS of MAs. Other statistical or experimental procedures in this manuscript mostly follow the approaches which have been developed in previous literature and thus show not much novelty.

Response:

We thank the reviewer for this positive assessment. Since evolutionary biology, population genetics, and model organism genetics are three of eLife’s major focus areas, we are hoping to communicate our results to this journal’s broad audience rather than restrict ourselves to a journal focusing too narrowly on just one of these focus areas.

Reviewer #3:

**Summary** The authors show that certain yeast strains have altered mutation rates/bias. The study is well motivated, genetic variation in mutation rates are not easily uncovered, and capitalizes on yeast and a high-throughput mutation rate/bias method that validates findings of C>A bias from yeast polymorphism data. The results are solid and clearly presented and I have no major concerns.

Response:

We are very grateful for this positive response. Please find our response to each minor comment below.

**Major comments** None

**Minor comments** Should have comma: "In addition, environmental ..."

Response:

We will fix this in revision.

Using S. paradoxus to classify derived vs ancestral alleles may not work as well as allele frequency. A 1/100 rare variant is 100x more likely derived than common variant. But with S. paradoxus divergence of say 5%, 5% polymorphic sites are misclassified or NA. Of course, since you used both, this is not a concern. But the number of variants included/excluded in each analysis should be reported. Also, I was a bit surprised that the rare variants are more noisy since most variants are rare.

Response:

We agree that the heuristic of classifying rare alleles as derived will do the right thing the majority of the time, but this could potentially create artifactual differences between the mutation spectra of different populations because the exact ratio of rare derived alleles to common derived alleles depends on the population’s demographic history and true site frequency spectrum. If two populations had the same mutation spectrum but very different proportions of variants that are polarized incorrectly, this could create the appearance of a mutation spectrum difference where none exists. In the revision, we will be sure to report the total number of variants filtered because of the variation present in S. paradoxus.

The reviewer is right to point out that rare variants are generally more abundant than common variants, but this pattern is much more pronounced in a species like humans that has undergone recent population expansion than it appears to be in S. cerevisiae, which appears to have a higher proportion of older, shared variation. We hope this clarifies why the rare variant mutation spectrum PCA appears noisier than the plot made from variation across more frequency categories.

In regards to variation in mutation rate based on canavanine resistanct. There is a caveat that some strains may be more canavanine resistant - due to differences in transporter abundanced or some other aspect of metabolism. Thus, the same mutation would survive and grow (barely) in one strain background, but not another. This caveat is very unlikely to have much of an impact but it would be worth discussing.

Response:

Thanks for pointing this out. We also considered the possibility that our mutation rate estimates could be confounded by slight differences in canavanine resistance between strains, and will address this point in the discussion.

The explanation for synonymous mutations is hitchhikers or errors. However, they could also disrupt translation, here's one possibility PMC4552401.

Response:

Thanks for pointing this out. We will expand our statement on the possible significance of synonymous mutations to include modification of transcription and translation efficiency.

Are there CAN allele differences between strains? If there are some, it might be worth mentioning why you do/don't think this influences the mutation rate. E.g. CGG is one step from stop but CGT is not.

Response:

The reviewer makes a good point that there are segregating differences among these strains in the sequence of CAN1. We plan to add an analysis where we calculate the number of opportunities for missense mutations and nonsense in each strain, as a function of its CAN1 sequence, to put a bound on the amount that these differences could affect our estimates of mutation rates in each strain.

For the allele counts in Figure 5B. 2 indicates a variant is present in one strain so there are only 9 mutations present in AAR and not found in ANY other strain or just not found in the four listed? Likewise AAR has 36 for count 4, meaning that there are 36 variants present in AAR and one other strain, where other strains are just the 4 shown in the table, or other strains being any of the 1011?

Response:

The allele count in Figure 5B represents the number of times the derived allele is present in the whole population. In this case, the whole population refers to the 1011 strains minus 336 strains that are so closely related to other strains in the panel that they are effectively duplicates. An allele of count 2 might be homozygous in AAR and absent from all other strains, or present as one heterozygous copy in AAR as well as one heterozygous copy in another strain. We will explain this more clearly in the revised manuscript.

"To our knowledge, this is one of the first" This is an odd way to put it and could be rephrased. As it stand you are either the first and not knowledgeable or knowledgeable and not the first.

Response:

Thanks. We will revise this to state that to our knowledge, we are the first to report such a discovery.

"humans, great apes, .." Could you put the citations in the discussion too. I was a little surprised there was no mention of C>A bias as it relates to studies in bacteria and cancer, where there has been a lot of work on mutational spectra. A comment on this literature or whether the C>A biases are not found elsewhere would be nice.

Response:

We will add citations and discussion of bacteria and cancer in the revised manuscript. The reviewer is right to point out that C>A mutations do come up in cancer signatures, for example in familial adenomatous polyposis disorders where excision repair of 8-oxoguanine is compromised.

Reviewer #3 (Significance (Required)):

I am an evolutionary geneticist with expertise in genomics and bioinformatics. In addition to reviewing papers I also regularly handle papers as an editor. The manuscript provides rare insight into population variation in mutation rates. While differences in mutational biases are well known between species and in some cases within a species, we typically don't know what causes this biases. Environmental factors are often thought to be involved; this work clearly shows that genetic (mutator strains) exist and impact polymorphism in yeast. The manuscript does a nice job in the introduction of explaining the background on mutation rate research and motivation for the work. It also clear explains the advantage of an experimental highthroughput mutation rate/spectra approach. Thus, I believe this new angle on a long-standing problem will be of interest to the community of evolutionary geneticists outside of yeast researchers.

Response:

We appreciate this very generous assessment, thank you!

Reference

Freeland, S. J. and Hurst, L. D. (1998) ‘The genetic code is one in a million’, Journal of molecular evolution, 47(3), pp. 238–248.

Lang, G. I. and Murray, A. W. (2008) ‘Estimating the Per-Base-Pair Mutation Rate in the Yeast Saccharomyces cerevisiae’, Genetics, 178(1), pp. 67–82.

Sharp, N. P. et al. (2018) ‘The genome-wide rate and spectrum of spontaneous mutations differ between haploid and diploid yeast’, Proceedings of the National Academy of Sciences of the United States of America, 115(22), pp. E5046–E5055.

Zhu, Y. O. et al. (2014) ‘Precise estimates of mutation rate and spectrum in yeast’, Proceedings of the National Academy of Sciences of the United States of America, 111(22), pp. E2310–8.

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Referee #3

Evidence, reproducibility and clarity

Summary

The authors show that certain yeast strains have altered mutation rates/bias. The study is well motivated, genetic variation in mutation rates are not easily uncovered, and capitalizes on yeast and a high-throughput mutation rate/bias method that validates findings of C>A bias from yeast polymorphism data. The results are solid and clearly presented and I have no major concerns.

Major comments

None

Minor comments

Should have comma: "In addition, environmental ..."

Using S. paradoxus to classify derived vs ancestral alleles may not work as well as allele frequency. A 1/100 rare variant is 100x more likely derived than common variant. But with S. paradoxus divergence of say 5%, 5% polymorphic sites are misclassified or NA. Of course, since you used both, this is not a concern. But the number of variants included/excluded in each analysis should be reported. Also, I was a bit surprised that the rare variants are more noisy since most variants are rare.

In regards to variation in mutation rate based on canavanine resistanct. There is a caveat that some strains may be more canavanine resistant - due to differences in transporter abundanced or some other aspect of metabolism. Thus, the same mutation would survive and grow (barely) in one strain background, but not another. This caveat is very unlikely to have much of an impact but it would be worth discussing.

The explanation for synonymous mutations is hitchhikers or errors. However, they could also disrupt translation, here's one possibility PMC4552401.

Are there CAN allele differences between strains? If there are some, it might be worth mentioning why you do/don't think this influences the mutation rate. E.g. CGG is one step from stop but CGT is not.

For the allele counts in Figure 5B. 2 indicates a variant is present in one strain so there are only 9 mutations present in AAR and not found in ANY other strain or just not found in the four listed? Likewise AAR has 36 for count 4, meaning that there are 36 variants present in AAR and one other strain, where other strains are just the 4 shown in the table, or other strains being any of the 1011?

"To our knowledge, this is one of the first" This is an odd way to put it and could be rephrased. As it stand you are either the first and not knowledgeable or knowledgeable and not the first.

"humans, great apes, .." Could you put the citations in the discussion too. I was a little surprised there was no mention of C>A bias as it relates to studies in bacteria and cancer, where there has been a lot of work on mutational spectra. A comment on this literature or whether the C>A biases are not found elsewhere would be nice.

Significance

I am an evolutionary geneticist with expertise in genomics and bioinformatics. In addition to reviewing papers I also regularly handle papers as an editor. The manuscript provides rare insight into population variation in mutation rates. While differences in mutational biases are well known between species and in some cases within a species, we typically don't know what causes this biases. Environmental factors are often thought to be involved; this work clearly shows that genetic (mutator strains) exist and impact polymorphism in yeast. The manuscript does a nice job in the introduction of explaining the background on mutation rate research and motivation for the work. It also clear explains the advantage of an experimental highthroughput mutation rate/spectra approach. Thus, I believe this new angle on a long-standing problem will be of interest to the community of evolutionary geneticists outside of yeast researchers.

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Referee #2

Evidence, reproducibility and clarity

Mutation is a fundamental force in organismal evolution, and therefore understanding the evolution of mutational mechanisms are important in evolutionary studies. In this manuscript, the authors used strains of S. cerevisiae as a model system to study the variations of rates and spectra in mutations with bioinformatic and experimental approaches. First, the authors analyzed the polymorphism data from 1011 strains by PCA analysis and show the variations in spectra. Second, the authors used fluctuation test combined with deep sequencing of the resistance gene to identify mutation rates and spectra in 18 strains, which show ~10-fold mutation rate variations and increased C-to-A mutations in two strains.

For the second part, the experimental procedures and statistical analysis are mostly solid. For the first part, as what authors said in the introduction, polymorphism is not equal to the mutation spectra. I think the authors did a good job by being cautious in the wording and having no over-inference after the analysis. It is thus inevitable that the conclusion of this part sounds mostly descriptive. The overall writing is very clear. I will recommend the publication in field-specific journals.

Minor comments:

P9 - It is very hard to not wonder how the 16 strains were picked in the fluctuation tests. Some comments on that will be appreciated. E.g., was that informed by the results of Fig 1?

P17- In the paragraph "natural selection might contribute ..." , is there any example of "certain mutation types are more often beneficial than others"?

P20 - Extra ')' in the sentence "Adjacent indels were merged if their frequencies differed by less than 10%)." In the discussion, it might be good to add a paragraph to compare the rate and spectra reported here and the ones found by MA and then NGS approach(e.g., Zhu et al. 2014).

Significance

The significance of this manuscript will be relatively specific to evolutionary biologists and geneticists, especially those who use yeasts as a model system. For example, I expect the variation of mutation rates and spectra found in this manuscript will impact the following population-genetic analysis in this collection of 1011 strains and motivate more studies on the molecular machineries which affect mutation rates and spectra.

In addition, in terms of methodological novelty, adding a novel step of reporter-gene sequencing is a reasonable way to get some information on mutation spectra as it is less labor-intensive than NGS of MAs. Other statistical or experimental procedures in this manuscript mostly follow the approaches which have been developed in previous literature and thus show not much novelty.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The authors describe a useful modified fluctuation assay that couples conventional mutation rate analysis with mutational spectrum characterization of forward mutations at the S. cerevisiae CAN1 locus. They nicely showed that wild yeast isolates display a wide range of mutation rates with strains AAR and AEQ displaying rates ~10-fold higher than the control lab strain. These two strains also showed a bias for C>A mutations, and were the only strains analyzed that had a mutation spectrum statistically different from the lab control. Together, these data provide a compelling proof-of-principle of the applicability of the modified fluctuation analysis approach described in this manuscript. Overall, the manuscript is very well written, and the work reported in it does represent a valuable contribution to the field. However, two primary shortcomings were identified that can be addressed to strengthen the conclusions prior to publication. Both points described below pertain to the analysis of the possible C>A specific mutator phenotype in strains AAR and AEQ.

Major comments:

1. The work presented in the manuscript does suggest that these two haploids are likely to display the C>A mutator phenotype. Yet, the authors fell short of providing a full and unambiguous demonstration that would elevate the significance of their discovery. They could have directly tested the predicted C>A specific mutator phenotype by conducting additional experiments, one of which is relatively simple. Specifically, they could have performed a simple reversion-based mutation assay to validate the reported C>A mutator phenotype displayed by AAR and AEQ. For example, into AAR, AEQ, and a wild type control, the authors could introduce an engineered auxotrophic marker allele (e.g., ura3 mutation) caused by an A to C substitution, which upon mutation back to A restores prototrophic growth in minimal media (ie. reversion from ura3-C to URA3-A). Such specific reversible allele should be relatively easy to integrate into the AAR and AEQ genomes, as well as in the control strain. Based on the authors' prediction, AAR and AEQ should display a very large increase (far higher than 10 fold) in the reversion rate when compared to a control haploid. To demonstrate the specificity of the mutation spectrum, the authors could test the reversion rates of a different engineered allele requiring a reversion mutation in the opposite direction (ie. reversion from ura3-A to URA3-C). If the AAR and AEQ mutator is specific C>A, one would predict that all three strains should have similar mutation rates for a reversion in the A>C direction. This additional genetic work would thoroughly validate the central discovery and would reinforce the usefulness of the method described in the manuscript.

Alternatively, a conventional mutation accumulation and whole genome re-sequencing experiment with parallel lines of AAR, AEQ and a control strain would also very effectively validate the C>A mutator prediction, and it would also answer the authors' discussion point about specificity to the CAN1 locus. However, it would be more costly and much more time consuming.

1. The second concern is in regard to the relatively extensive conclusions drawn about the possible evolutionary significance of the possible C>A mutator in AAR and AEQ. The authors should be more cautious and conservative in the proposed interpretation. As the authors note:

'Three of the four C>A-enriched mosaic beer strains, AAR, AEQ, and SACE_YAG, are all haploid derivatives of the [highly heterozygous] diploid Saccharomyces cerevisiae var diastaticus strain CBS1782, which was isolated in 1952 from super-attenuated beer.'

From this statement, and because the paper cited provided few details on the isolation of CBS1782, it is presumed that these haploid derivatives were most likely isolated as recombinant spores. Furthermore, it is unclear when this isolation occurred, and for how many generations strains AAR and AEQ have been propagated in a haploid state.

Herein lies a critical point: AAR and AEQ were recently derived from a diploid background with a "high level of heterozygosity". In a heterozygous diploid context, deleterious point mutations (and any resulting mutator phenotypes) would likely be masked by the presence of wild-type alleles. Now, as haploids, they express a novel genotype (i.e., combination of defective or incompatible parental alleles), which manifests as a mutator phenotype. In this respect, AAR and AEQ appear analogous to the spore derivatives of the incompatible cMLH1-kPMS1 isolate referred to in the manuscript as a notable exception. The analysis of strains harboring incompatible MLH1-PMS1 mutations by Raghavan et al. demonstrated that the heterozygous diploid parents were not themselves mutators, but that haploid spores which had inherited the pair of incompatible alleles displayed mutator phenotype. Collectively, while it can certainly be argued that the strains AAR and AEQ (like the MLH1/PMS1 incompatible strains) are mutators now, this fact alone does not support the conclusion that they have adapted to survive the expression of an extant mutator phenotype. This premise could be tested by analyzing the mutation rates/spectra of four new spores derived from a single tetrad of CBS 1782. Do the four sibling spores display similar or different mutational rates and spectra? If all four spores from a single tetrad exhibit the 10-fold increase in CAN1 mutation rate and the C>A transversion bias, then it can be inferred that the diploid parent is also a mutator in the same manner. Further direct analysis of mutation rates and spectrum in the parent diploid CBS 1782 would complete the work. This finding would be quite significant, and would provide strong evidence that wild strains can in fact tolerate the expression of a chronic mutator allele.

Minor comments:

A final, relatively minor point. That the new haploids AAR and AEQ show distinct mutation rates and spectra opens the door to an interesting line of inquiry, which may help to identify the causative mutator allele in a manner more efficient than searching for missense mutations. It is stated, and it is understandable, that the identification of the possible causal mutations is beyond the scope of the present manuscript. In this spirit, it would be much more appropriate to restrict such considerations to the Discussion section. Specifically, while the authors make a plausible case for OGG1 being a candidate gene responsible for the C>A mutator phenotype, no experimental demonstration was attempted. As such, that text segment should be moved from the Results to the Discussion section.

Significance

As stated in the summary section above, the manuscript by Jiang et al represents a substantial contribution to the fields of genome stability and genome evolution. The method described is likely to be useful beyond budding yeast. The work will be appreciated by a broad audience of geneticists. The additional work and text modifications proposed above would likely further elevate the impact of this work.

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Reply to the reviewers

Answers to the reviewers’ comments

We deeply appreciate the reviewers for their thoughtful, critical and constructive comments, which have undoubtedly provided us with valuable opportunities to improve our manuscript.

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

Extravasation of lymphocytes from HEV in the lymph nodes is mediated by the interaction between lymphocyte L-selectin and PNAd-carrying sulfated sugars expressed by HEVs. Multiple steps of lymphocyte migration interacting with ECs at the luminal side of HEVs have been studied intensively; however, post-luminal migration steps are unclear. In this study, using intravital confocal microscopy of peripheral lymph nodes (pLNs), the authors found that GlcNAc6ST1 deficiency, required for sulfation of PNAd, delays trans-fibroblastic reticular cell (FRC) migration of lymphocytes, and hot spots of trans-HEV EC migration and trans-FRC migration. Interestingly, hot spots of trans-FRC migration are often associated with dendritic cells (DCs). Thus, the authors concluded that FRCs delicately regulate the transmigration of T and B cells across the HEV wall, which could be mediated by perivascular DCs.

**Main comments**

1. This study focused on pLNs, which are quite different from mesenteric lymph nodes (mLNs) in many ways. The authors should include mLNs in their study to make the general statement with regard to the T/B cell entry into lymph nodes. In addition, it will be more significant if this study includes challenged pLNs.

We thank the reviewer for raising the important point. We agree that mesenteric lymph nodes are quite different from peripheral lymph node that this study focuses on. Therefore, we specified the popliteal or peripheral lymph node in the revised manuscript as follows.

In the Abstract (page 2), “… Herein, we performed intravital imaging to investigate post-luminal T and B cell migration in popliteal lymph node, consisting of trans-EC migration, crawling in the perivascular channel (a narrow space between ECs and FRCs) and trans-FRC migration. … These results suggest that HEV ECs and FRCs with perivascular DCs delicately regulate T and B cell entry into peripheral lymph nodes.”

In the Introduction (page 4), “Herein, we clearly visualized the multiple steps of post-luminal T and B cell migration in popliteal lymph node, including trans-EC migration, intra-PVC crawling and trans-FRC migration, using intravital confocal microscopy and fluorescent labelling of ECs and FRCs with different colours.

In the Discussion (page 21), “… These results imply that pericyte-like FRCs, the second cellular barrier of HEVs, regulate the entry of T and B cells to maintain peripheral lymph node homeostasis more precisely and restrictively than we previously thought.”

In addition, we discussed the difference in lymphocyte migration across HEVs between peripheral lymph node, mesenteric lymph node, and peyer’s patches in the Discussion of the revised manuscript. We also discussed inflamed lymph nodes in the Discussion as follows.

In the Discussion (page 20), “… Although this work focused on peripheral lymph node, the other lymphoid organs have different lymphocyte homing efficiency61 due to organ-specific gene expression on HEVs62. B cells home better to mesenteric lymph nodes and peyer’s patches than peripheral lymph nodes61 by CD22-binding glycans expressed preferentially on the HEVs of mesenteric lymph nodes and peyer’s patches62.

Inflamed peripheral lymph node become larger by recruiting more lymphocytes and even L-selectin-negative leukocytes that are excluded in the steady state63,64. Inflamed HEV ECs show different gene expression, such as downregulation of GLYCAM1 and GlcNAc6ST-160. In addition, inflamed HEV integrity may be loosen due to markedly increased leukocyte influx although the HEV FRCs can prevent bleeding by interacting with platelet CLEC-248. CD11c+ DCs are associated with inflamed HEV EC proliferation that is functionally associated with increased leukocyte entry65. The stepwise migration of lymphocyte across inflamed HEVs and their hot spots with perivascular CD11+ DCs will be interesting topic for future study.”

The finding that GlcNAc6ST1 deficiency delays lymphocyte trans-FRC migration but not trans-HEV EC migration is surprising. However, the reason this occurs is neither shown nor discussed. Is GlcNAc6ST1 also expressed in FRCs? Or does GlcNAc6ST1 expression on HEV license lymphocytes to transmigrate across FRCs?

This is valid point to be addressed. GlcNAc6ST-1 is predominantly involved in PNAd expression on the abluminal side rather than on the luminal side. Therefore, our results that GlcNAc6ST-1 deficiency increased the time required for trans-FRC migration but not that for trans-EC migration, could be attributable to deficiency of GlcNAc6ST-1-synthesizing L-selectin ligands in the abluminal side of HEV.

In addition to PNAd expression in the luminal and abluminal sides of endothelial cells in HEV, PNAd expression has been observed in reticular network close to HEV as following figures. We believe that PNAds are expressed in FRCs close to HEV and can affect lymphocyte migration such as trans-FRC migration and parenchymal migration. By looking at the data (Table S1, Rodda et al., Immunity 2008), GlcNAc6ST-1 (Chst2) is expressed in T-cell-zone reticular cells while GlcNAc6ST-2 (Chst4) is absent. Therefore, it is presumable that FRC-expressed GlcNAc6ST1 may regulate trans-FRC migration in some extent.

Figures. PNAD expression on HEVs (arrows) and reticular network (arrow heads) close to the HEVs

We included these points in the Discussion of the revised manuscript (page 15) as follows.

“… GlcNAc6ST-1 is predominantly involved in PNAd expression on the abluminal side rather than on the luminal side, although GlcNAc6ST-1 deficiency also modestly affects the luminal migration of lymphocytes by increasing the rolling velocity9. GlcNAc6ST-1 deficiency increased the time required for trans-FRC migration but not that for trans-EC migration. This could be attributable to deficiency of GlcNAc6ST-1-synthesizing L-selectin ligands in the abluminal side of HEV. In addition to the abluminal side of HEV endothelial cells, FRCs also express GlcNAc6ST-1, but not GlcNAc6ST-227, implying that FRC-expressed GlcNAc6ST-1 may regulate trans-FRC migration in some extent. … Thus, PNAds expressed at the endothelial junction and on the abluminal side of HEVs facilitate the efficient transmigration of lymphocytes across the HEV wall but do not slow transmigration in the perivascular region. GlcNAc6ST-1 deficiency and MECA79 antibody also decreased the parenchymal B and T cell velocities immediately after extravasation, respectively, probably because of blockade of parenchymal expression of PNAd in close proximity to HEV6,21,28.”

Because of the adoptive transfusion experiment, the actual number of transmigrating lymphocytes in Fig. 3F is underestimated.

We agree with the reviewer’s comment. We corrected the y-axis label in Fig. 3F from ‘average number of cells transmigrating at one site’ to ‘average number of labeled cells transmigrating at one site.’

Whether DCs covering FRCs have a role for lymphocyte trans-migration is not shown.

We leaved this work as future research and discussed about the potential mechanisms in the Discussion (page 17-18) that the DC may regulate lymphocyte entering by interacting FRC with LTβR or CLEC-2 signaling. We also included ‘Martinez et al Cell Rep 2019 (ref.51)’ in the discussion of the revised manuscript (page 18). In addition, we also discussed about better characterization of the CD11c+ DC in the Discussion of the revised manuscript (page 19) as follows.

In the Discussion (page 18), “The podoplanin of FRCs also controls FRC contractility49,50 and ECM production51 by interacting with the CLEC-2 of DCs in inflamed lymph nodes. In the steady state, resident DCs in lymph nodes express CLEC-252. Thus, it is conceivable that CLEC-2+ resident DCs may control the contractility of FRCs and remodel ECM surrounding HEVs to facilitate the trans-FRC migration of T and B cells. Thus, the CLEC-2/podoplanin signalling may represent a key molecular mechanism underlying our discovery that trans-FRC migration hot spots preferentially occur at FRCs covered by CD11c+ DCs.”

In the Discussion (page 19), “… In addition, better characterization of the CD11c+ DCs located in the hot spots of HEVs is required to differentiate them from the other CD11c+ DCs observed in the non-hot-spot regions of HEVs. Some T-cell-zone resident macrophages can also express CD11c54. Imaging of a triple-transgenic mouse with Zbtb46-cre;tdTomato and CD11b-GFP will be able to differentiate 3 types of DCs and macrophages potentially associated with the hot spots: Zbtb46+CD11b- cDC1, Zbtb46+CD11b+ cDC2, and Zbtb46-CD11b+ macrophage54,55.”

In Fig. 1, time required for trans HEV EC migration and trans-FRC migration of T cells is shorter than that of B cells; however, this finding is not observed in Fig. 2C and E.

Although the statistical comparison between T and B cells are not shown in Fig. 2C-F and S5., there are actually significant difference between T and B cells, which are similar results as Fig. 1 except for the dwell time in PVC. P values between T and B cells in wildtype mice are 0.0003, In the Result (page 6), “… The mean velocity of T cells (5.3 ± 1.7 μm/min) was significantly higher than that of B cells (4.1 ± 1.4 μm/min) during intra-PVC migration (Fig. 1E), while the dwell time and total path length in the PVC were not significantly different between T and B cells (Fig. 1, H and I). Similar results were obtained when both cells were imaged simultaneously, except that B cells had significant longer dwell time than T cells (Fig. 2C-F and Fig. S5). Interestingly, more than half of the T and B cells crawled from 50 μm to 350 μm inside the PVC (Fig. 1I), …”

In the legend of Fig. 2, “… P values between T and B cells in wild-type mice were 0.0003 (C), …”

In the legend of Fig. S5, “… P values between T and B cells in wild-type mice were 0.0240 (A), 0.3614 (B), 0.7518 (C) and 0.1337 (D). …”

**Minor comments**

1. Please provide evidence for GlcNAc6ST1 deficiency in HEV and surrounding tissues.

Previous studies (Uchimura et al., JBC 2004, Nat. Immunol. 2005; ref9 and 10, respectively, in the manuscript) confirmed systemic deficiency of GlcNAc6ST-1 in peripheral lymph nodes of the GlcNAc6ST-1 KO mice.

Images for delayed trans-FRC migration in GlcNAc6ST1 KO mice relative to WT are not convincing (Fig. 2G and H).

We think the reason why the images look unconvincing is probably because it is not easy to quickly determine the images corresponding to the trans-FRC migration in the image sequence. To make the transmigration images easier to recognize, we added arrow heads indicating the transmigration site in Fig. 2G and 2H, and Fig. S4 as follows.

Provide actual time periods required for Fig. 3F and G. Lack of isotype control IgG experiment in Fig. S3.

We added the time periods (3 hours) in the figure legend as follows.

“… (F) Average numbers of labeled T and B cells transmigrating at one site for 3 hours. (G) Ratio of hot spots to total transmigration sites for 3 hours. …”

The purpose of Fig. S3 was to confirm that the anti-ER-TR7 antibody injection for labeling FRC do not alter normal T cell motility, rather than to confirm the function of ER-TR7. Therefore, we used non-injected group as control rather than control antibody injection group.

Line 12 on page 11, "the ratio of hot spots to the total “observed” transmigration sites..." is not appropriate. The ratio must be calculated by hot spots to the total "potential" transmigration sites, although it is challenging to find total potential sites.

We corrected the expression from ‘the total observed transmigration sites’ to ‘the total potential transmigration sites’.

Please correct typos of angiomoduin to angiomodulin (page 16), ET-TR7 to ER-TR7 (page 17), Anti-CD3 to anti-CD3 (page 22), half the dose to half dose (page 22), the Multiple step to the multiple step (page 23).

We thank the reviewer for finding those errors. We corrected them and performed proofreading repeatedly to correct typos and grammatic errors.

Please provide an additional explanation of why actin-DsRed in HEVs is more strongly expressed than surrounding tissues such as FRCs in Fig. 1 although actin-DsRed should be expressed in all cell types in mice.

We were also surprised when we found that HEV ECs expressed red fluorescence more strongly compared to surrounding tissues. Although the other cells such as FRCs and endogenous lymphocytes also express DsRed under control of a promotor gene, beta-actin, we believe that HEV ECs express more strongly, which is sufficient to image only HEV-EC by adjusting an image contrast. We revised the explanation of this point in the Methods (page 21) as follows.

“HEV ECs of actin-DsRed mouse popliteal lymph node expressed red fluorescence much stronger than the surrounding stromal cells and endogenous lymphocytes, which was sufficient to image only HEV ECs by adjusting an image contrast (Fig. 1, A and B).”

Reviewer #1 (Significance (Required)):

The study focused on lymphocytes post extravasation of HEV, which is an understudied question, using intravital imaging. The in vivo imaging study was deliberately and beautifully performed, and the finding is insightful for understanding lymphocyte trafficking in lymph nodes. However, additional experimental should be performed to address some weaknesses listed in our comments.

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

The present study by K. Choe meticulously monitored the stepwise transmigration behavior of T cells and B cells, respectively, through the high endothelial venules of the mouse popliteal lymph node using the laser scanning confocal microscopy. In particular, the study focused on the post-luminal migration of T and B cells and reported the following. (1) Mice deficient in GlcNAc6ST-1 which is necessary for PNAd expression on the abluminal side of HEV showed significantly reduced abluminal migration of both T and B cells, (2) the footpad injection of the ER-TR7 antibody did not affect T cell transmigration across HEVs but marginally increased the parenchymal T cell velocity when compared with injection of control antibody, (3) T cells and B cells tended to share FRC migration hot spots but this was not the case with trans-EC migration hot spot, (4) the trans-FRC migration was observed at the FRCs closely associated with CD11c+ dendritic cells in HEV.

While the present study is obviously the product of very meticulous and time-consuming work, it basically describes only a phenomenology, just reporting the lymphocyte behavior within and outside lymph node HEVs, without sufficiently analyzing the mechanistic aspect of the individual event they observed. The only antibody blocking experiments they performed to obtain mechanistic insights was by the use of commercially available monoclonal antibodies, all of which unfortunately contained a preservative, sodium azide, which potently blocks lymphocyte migration in vivo (Freitas AA & Bognacki J, Immunol 36:247, 1979). Therefore, the results of these antibody blocking experiments cannot be taken at face value.

We thank the reviewer for raising the important point. Freitas et al used pre-treated lymphocytes with sodium azide in vitro for 1 hour while we injected the antibody into the footpad of recipient mouse 3 hours before lymphocyte injection via tail vein and imaging. Sodium azide might be highly diluted in vivo condition. In addition, Fig. S3 shows no significant difference in T cell migration in HEV between anti-ER-TR7 antibody-injected and non-injected groups although the anti-ER-TR7 antibody also contains sodium azide. We believe that the effect of sodium azide on our convincing results of the PNAd-blocking antibody compared to the control antibody (Fig. S8) may be insignificant. The potential side effect of sodium azide was mentioned in the Methods of the revised manuscript (page 22) as follows.

“All antibodies we used contains sodium azide that has potential side effects on lymphocyte migration in lymph node57. However, Fig. S3 shows no significant difference in T cell migration in HEV between anti-ER-TR7-injected and non-injected groups.”

Reviewer #2 (Significance (Required)):

Real time imaging experiments were performed very carefully. However, as mentioned above, authors used sodium azide-containing antibodies for blocking experiments, and hence, these experiments cannot be interpreted properly.

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

This study presents a detailed investigation of T and B cell entry into lymph nodes (LN) via HEV. Substantial high quality intravital imaging is used to examine trans-EC and trans-FRC migration and define the role of PNAds in this process. The authors find that T and B cells use 'hot spots' to cross EC and FRC barriers, which supports prior similar observations by others. They also show that where T and B cells cross EC and FRC layers can differ, with regions of shared trans-FRC migration but more distinct EC crossing sites. This may relate to differences in the structure of these cellular layers, but provides novel insight into the mechanisms of cell entry into LNs via HEV. Assessment of the dependence on PNAd using antibodies or GlcNAc6ST-1 KO mice revealed perivascular and parenchymal cell behavior is also influenced by these signals. Lastly, examination of DCs that sit on the perivascular FRCs suggested that cells may prefer to cross at sites co-localized by DCs, although the reasons for this are not explored.

This is a well performed study, with high quality imaging data and analysis. The results are convincing, with sufficient numbers of mice and adequate statistical analysis. There are a number of minor grammatical errors throughout the text, which should be easy to fix.

We thank the reviewer for the positive evaluation. We carefully performed proofreading repeatedly to correct typos and grammatical errors.

Reviewer #3 (Significance (Required)):

Although 'hot spots' have been proposed by others, this detailed analysis provides new knowledge of how lymphocytes can cross the HEV and FRC barriers to enter LNs. This is an important study to advance our understanding of cell recruitment to lymph nodes. The role of perivascular and parenchymal PNAd signals observed here should also be of interest to immunologists to help define the signals required for immune cell motility in tissues.

Reviewer #4 (Evidence, reproducibility and clarity (Required)):

The authors have used a combination of intravital confocal imaging and transgenic models to study the migration of T and B cells through the HEVs. They move on from Moscacci et al. and Park et al., studies on lymphocyte migration. This study focuses on visualization and molecular mechanism of post-trans-EC migration, including the intra-PVC and trans-FRC migration of T and B cells in HEVs. They have been able to show how lymphocytes migrate through the HEV into the parenchyma. Using the GlcNAc6sT-1 (catalyst for sulfation of PNAds) KO model (and MECA control for PNAds blocking) they identify the role of L-selectin/PNAd for lymphocyte transmigration. The identification of hot spots of T and B cell transmigration in HEVs is novel and extremely interesting for the field however the data shown is not entirely convincing in their current form. The hot spots were defined as areas where the lymphocytes migrate through the HEV epithelial cells and pericyte (FRC) regions. These are areas where migration was greatly shared T and B cells. Using the CD11c-YFP mouse model they identified CD11c+ cells in proximity to the FRCs located at the migration hotspots which can drive further speculation regarding the mechanism by which these areas of the HEVs are more permissive.

**Major comments**

1) Intravital imaging of T and B cell transmigration across HEVS composed of ECs and FRCs

• Figure 1: The authors mention that they performed similar experiments for B cells. Authors should show comparative data for T cells and B cells.

• Panel S1B should be provided for both T and B cells in figure 1.

We added the image sequence of B cell migration and the panels (Fig S1B of previous manuscript) showing intra-PVC segments of T or B cells in Fig. 1C of the revised manuscript as follows.

2) T and B cells preferentially share hotspots for trans-FRC migration not EC-migration

• Figure 4: This data is important to the storyline but as presented it is difficult to understand. Results are overstated in the text however it is difficult to see where these conclusions come from based on the figure. In Figure 4B the authors should show percentages on the Venn diagram or remove it entirely. In Figure 4C the authors should add labels to their y-axis and separate the data in order to assist with the storyline and convince of the presence of hot spots.

We agree with the reviewer’s opinion. We removed the Venn diagram, separated the Fig. 4C into 4B and 4C, and added y-axis labels in the figures. In addition, we revised the figure legends and the text in the Results to make it easier to understand as follows.

In the figure legend, “…(B-C) The round and diamond symbols represent predicted and observed values, respectively, for the percentage of T cell hot spots in B cell hot spots (B), for the percentage of B cell hot spots in T cell hot spots (C). …”

In the Results (page12), “Simultaneously imaging T and B cells showed that some T and B cells transmigrated across FRCs at the same site (Fig. 4A and Movie S8). To investigate whether T and B cells share their hot spots preferentially or accidentally, we compared the percentage of T cell hot spots in total B cell hot spots (diamond symbols in Fig. 4B) with its predicted value that is the possibility of accidently sharing T and B cell hot spots (round symbols in Fig. 4B). The predicted value can be calculated as the percentage of T cell hot spots in total transmigration sites. To note, the percentage of hot spots in total sites for trans-FRC migration was higher than that for trans-EC migration (Fig. 3G and round symbols in Fig. 4B) maybe because the number of trans-FRC migration sites was less than that of trans-EC migration sites. It implies that the possibility of accidently sharing T and B cell hot spots for trans-FRC migration is higher than that for trans-EC migration. However, surprisingly, the percentage of T cell hot spots in B cell hot spots was significantly higher than its predicted value of accidently sharing hot spots for trans-FRC migration (Fig. 4B). Similarly, the percentage of B cell hot spots in T cell hot spots was also significantly higher than its predicted value for trans-FRC migration (Fig. 4C). These results imply that T and B cells preferentially share trans-FRC migration hot spots beyond the prediction for accidently sharing. However, there were no significant differences between observed and predicted values for trans-EC migration (Fig. 4B and 4C), which implies T and B cells just accidently share their trans-EC migration hot spots.”

3) T and B cells prefer to transmigrate across FRCs covered by perivascular CD11c+ DCs

• DCs drive changes to FRC phenotype and contractility. The interaction between CLEC-2 (on DCs and platelets) is important for driving permeability of the HEVs. The authors use the CD11c-YFP mouse model in Figure 5 (and the supporting figures) to show the proximity of the CD11c+ cells and FRCs. Data from Baratin et al., (Immunity, 2017) suggest that CD11c+ cells in the parenchyma are also T cell zone macrophages (TZMs) that were previously characterized as DCs. Macrophages have previously been shown important for perivascular transmigration of neutrophils during bacterial skin infection (Abtin et al.2014- Nat Immun). CD11c-YFP alone does not show the cells proximal to FRCs are DCs so the authors should try to stain them with CLEC-2 or use the CLEC9a-cre mouse model to better characterise these cells.

We thank the reviewer for raising important point. We agree that the perivascular CD11c+ cells could be T-cell-zone macrophages (TZMs). Better characterization of the CD11c+ cells located in the hot spots of HEVs is required to determine if they are DCs or macrophages, and also to differentiate them from the other CD11c+ cells observed in the non-hot-spot regions of the HEVs. To differentiate DCs from TZMs, Zbtb46-GFP mouse can be used for imaging because Zbtb46-GFP are highly expressed in conventional DCs (cDCs) but not monocytes, macrophages, or other lymphoid or myeloid lineages (Satpathy et al, JEM 2012). However, endothelial cells also express Zbtb46-GFP. To visualize only DCs in HEVs, we need to make a chimeric mouse by adoptive transfer of Zbtb46-GFP bone-marrow cells into irradiated wild-type mouse. Furthermore, using a triple transgenic mouse with Zbtb46-cre;tdTomato and CD11b-GFP will be able to differentiate 3 types of DCs and TZMs potentially associated with the hot spots: Zbtb46+CD11b- cDC1 (red), Zbtb46+CD11b+ cDC2 (yellow), and Zbtb46-CD11b+ macrophage (green). However, since generation or obtaining of those transgenic mice models including CLEC9a-cre mouse will take long time, we will leave this work as future research and discussed this point in the Discussion of the revised manuscript as follows. In addition, we think that it will be difficult to differentiate the CLEC2 of perivascular DCs from that of platelets by in vivo labeling by injection of anti-CLEC2 antibody conjugated with a fluorescent dye because the CLEC2 of platelets maintains HEV integrity with interacting of FRC podoplanin (Herzog et al, Nature 2013).

In the Discussion (page 19), “… In addition, better characterization of the CD11c+ DCs located in the hot spots of HEVs is required to differentiate them from the other CD11c+ DCs observed in the non-hot-spot regions of HEVs. Some T-cell-zone resident macrophages can also express CD11c54. Imaging of a triple-transgenic mouse with Zbtb46-cre;tdTomato and CD11b-GFP will be able to differentiate 3 types of DCs and macrophages potentially associated with the hot spots: Zbtb46+CD11b- cDC1 (red), Zbtb46+CD11b+ cDC2 (yellow), and Zbtb46-CD11b+ macrophage (green)54,55.”

**Minor comments**

1) Intravital imaging of T and B cell transmigration across HEVS composed of ECs and FRCs

• The velocity differences observed could be due to location of HEV in the parenchyma. Furthermore, FRC plasticity can cause differences in secretion of chemokine gradients based on the location of cells and their niche (Rhoda et al., Immunity 2018). HEVs regulation of lymphocyte entry can be influenced by their niche (Veerman et al., Cell Reports 2019). The authors should comment on the HEV position relative to B cell areas.

We included this point with the references (Rhoda et al, immunity 2018, ref 27; Veerman et al., Cell Rep. 2019, ref 60) in the Discussion of the revised manuscript (page 19-20) as follows.

“Compared to T cell, B cells took a longer time to pass EC and FRC layers in HEV and had lower velocity in PVC and parenchyma just after extravasation. Furthermore, the adhesion rate of B cells to HEV EC in luminal side is lower than that of T cells5. These could be attributed to lower expression of L-selectin and CCR7 on B cells than T cells18,59. The difference in homing efficiency between T and B cells may vary depending on the HEV location due to the heterogeneous expression of chemokines and integrins on HEV EC and surrounding FRCs in peripheral lymph node27,60. The HEVs imaged in this work were located around 40-70 μm depth from the capsule where might be close to B cell follicles. B cell homing efficiency in the deeper paracortical T cell zone could be different from our data probably due to less CXCL13 that is chemoattractant for B cells highly expressed in follicles. …”

• Images shown in Fig1A is the same as Fig S1A/B. I presume this is an error.

Fig. 1A and Fig. S1A correspond to a 20-um-thick maximum intensity projection and single z-frame without projection, respectively. To avoid the confusion, we changed Fig.1A to the single z-frame (Fig S1A) and remove the 20-um thick maximum projection.

• Figure S3: Data for Ab treated appears to be identical to what is shown for T cells in Fig 1. I presume this is an error and the correct control will be shown.

We used the data of Fig. 1D-1I as the Ab-injected group in Fig. S3. We are sorry for the lack of clear explanation about this. We included the explanation in the figure legend as follows.

In the legend of Fig. S3, “(A-E) There is no significant difference between antibody-injected group (Ab) and non-injected group (Non) in T cell migration from trans-EC migration to trans-FRC migration. Non-injected means that no substance is injected into a footpad of mouse. We used the data of Fig. 1D-1I as the antibody-injected group. …”

2) Non-redundant role of L-selectin/PNAd interactions in post-luminal migration of T and B cells in HEV

• Could the authors clarify the number of mice used for this analysis (same applies to figure 1)

In the legends of Fig. 1-2, S6 and S8, there is the number of mice we used. In Fig. 1, “Four and 3 mice were used for the analysis of T and B cells, respectively.” In Fig. 2, “Four mice were analysed for each group.” In Fig. S6, “Three mice were analysed for each group.” In Fig. S8, “Five and 4 mice were analysed for the control Ab and MECA79 groups, respectively.”

In addition, we added the number of mice in the legend of Fig. S7. In Fig. S7, “The images are representative of 4 popliteal lymph nodes of 2 mice and 2 popliteal lymph nodes of a mouse for MECA79 and control IgM antibody, respectively.”

• Figure S6: further to percentages of T cell populations the authors should also provide the number of T cells (CD4, CD8, CM and naive) for both wildtype and KO.

We included the analyzed cell number by FACS in Fig. S6 and revised the figure legend as follows.

In the Fig. S6, “… (B) Analyzed cell numbers by FACS for 3 control and 3 KO mice. (C) Percentage of each type of T cells in DsRed+ T cells. No difference in the percentage of homing central memory, Naïve CD4 and CD8 T cells between wild-type and KO mice. …”

**Methods** for the flow cytometry analysis could the details of how samples were processed (or reference) be provided.

We added the details in the Methods (page 24) as follows.

“Popliteal and inguinal lymph nodes were harvested and single-cell suspensions were prepared by mechanical dissociation on a cell strainer (RPMI-1640 with 10% FBS). Cell suspensions were centrifuged at 300g for 5 min. Erythrocytes in lymph nodes were lysed with ACK lysis buffer for 5 min at RT. Cell suspensions were washed and filtered through 40um filters. Non-specific staining was reduced by using Fc receptor block (anti-CD16/CD32). Cells were incubated for 30 min with varying combinations of the following fluorophore-conjugated monoclonal antibodies: anti-CD3e (clone 145-2C11, BD pharmigen), anti-CD4 (clone GK1.5, BD Pharmingen), anti-CD8 (clone 53-6.7, eBioscience), anti-CD44 (clone IM7, Biolegend) and anti-CD62L (clone MEL-14, eBioscience) antibodies (diluted at a ratio of 1:200) in FACS buffer (5% bovine serum in PBS). After several washes, cells were analyzed by FACS Canto II (BD Biosciences) and the acquired data were further evaluated by using FlowJo software (Treestar).

**References:** The discussion covers key references in the field, but more recent studies should be included. Some examples have been suggested in the comments sections. Key references missing that can help discussion/interpretation of the data include: 1) Veerman et al 2019, Cell reports. The data in that paper shows the heterogeneity of the HEV and different regulation of genes that control lymphocyte entry. This can also be linked to the comments above regarding section 1 and 2. 2) Rhodda et al 2018, Immunity that focuses on niche-associated heterogeneity of lymph node stromal cells. The authors should also include Webster et al., 2006, JEM which describes the role of DCs in regulating vascular growth in the lymph node.

We thank the reviewer for suggesting good references to discuss. We included the references #1 and #2 in the revised manuscript as we responded to the minor comment #1. We also cited Webster et al., JEM 2006 (as ref 65) in the Discussion of the revised manuscript (page 20) as follows.

“Inflamed peripheral lymph node become larger by recruiting more lymphocytes and even L-selectin-negative leukocytes that are excluded in the steady state63,64. Inflamed HEV ECs show different gene expression, such as downregulation of GLYCAM1 and GlcNAc6ST-160. In addition, inflamed HEV integrity may be loosen due to markedly increased leukocyte influx although the HEV FRCs can prevent bleeding by interacting with platelet CLEC-248. CD11c+ DCs are associated with inflamed HEV EC proliferation that is functionally associated with increased leukocyte entry65. The stepwise migration of lymphocyte across inflamed HEVs and their hot spots with perivascular CD11+ DCs will be interesting topic for future study.”

Reviewer #4 (Significance (Required)):

This paper asks important questions and can make a significant contribution to the field if all revisions are addressed. The authors identified PNAd as an important factor for T cell migration. Further to previous studies in the field suggesting non-random transmigration sites. The authors used intra-vital confocal imaging to identify how lymphocytes cross the epithelial cells and FRCs of the HEVs to migrate to the parenchyma. The authors identify hotspots used by lymphocytes to transmigrate. Finally, the authors show that CD11c+ cells are proximal to FRCs hotspots and might have a role in driving lymphocyte transmigration.

Audience: Lymphocyte/immune cell biology, stomal immunology, FRC and lymph node inflammation. My expertise: Stomal immunology, immunology, innate immunity

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Referee #4

Evidence, reproducibility and clarity

The authors have used a combination of intravital confocal imaging and transgenic models to study the migration of T and B cells through the HEVs. They move on from Moscacci et al. and Park et al., studies on lymphocyte migration. This study focuses on visualization and molecular mechanism of post-trans-EC migration, including the intra-PVC and trans-FRC migration of T and B cells in HEVs. They have been able to show how lymphocytes migrate through the HEV into the parenchyma. Using the GlcNAc6sT-1 (catalyst for sulfation of PNAds) KO model (and MECA control for PNAds blocking) they identify the role of L-selectin/PNAd for lymphocyte transmigration. The identification of hot spots of T and B cell transmigration in HEVs is novel and extremely interesting for the field however the data shown is not entirely convincing in their current form. The hot spots were defined as areas where the lymphocytes migrate through the HEV epithelial cells and pericyte (FRC) regions. These are areas where migration was greatly shared T and B cells. Using the CD11c-YFP mouse model they identified CD11c+ cells in proximity to the FRCs located at the migration hotspots which can drive further speculation regarding the mechanism by which these areas of the HEVs are more permissive.

Major comments:

1) Intravital imaging of T and B cell transmigration across HEVS composed of ECs and FRCs

• Figure 1: The authors mention that they performed similar experiments for B cells. Authors should show comparative data for T cells and B cells.
• Panel S1B should be provided for both T and B cells in figure 1.

2) T and B cells preferentially share hotspots for trans-FRC migration not EC- migration

• Figure 4: This data is important to the storyline but as presented it is difficult to understand. Results are overstated in the text however it is difficult to see where these conclusions come from based on the figure. In Figure 4B the authors should show percentages on the Venn diagram or remove it entirely. In Figure 4C the authors should add labels to their y-axis and separate the data in order to assist with the storyline and convince of the presence of hot spots.

3) T and B cells prefer to transmigrate across FRCs covered by perivascular CD11c+ DCs

• DCs drive changes to FRC phenotype and contractility. The interaction between CLEC-2 (on DCs and platelets) is important for driving permeability of the HEVs. The authors use the CD11c-YFP mouse model in Figure 5 (and the supporting figures) to show the proximity of the CD11c+ cells and FRCs. Data from Beratin et al., (Immunity, 2017) suggest that CD11c+ cells in the parenchyma are also T cell zone macrophages (TZMs) that were previously characterised as DCs. Macrophages have previously been shown important for perivascular transmigration of neutrophils during bacterial skin infection (Abtin et al.2014- Nat Immun). CD11c-YFP alone does not show the cells proximal to FRCs are DCs so the authors should try to stain them with CLEC-2 or use the CLEC9a-cre mouse model to better characterise these cells.

Minor comments:

1) Intravital imaging of T and B cell transmigration across HEVS composed of ECs and FRCs

• The velocity differences observed could be due to location of HEV in the parenchyma. Furthermore FRC plasticity can cause differences in secretion of chemokine gradients based on the location of cells and their niche (Rhoda et al., Immunity 2018).HEVs regulation of lymphocyte entry can be influenced by their niche (Veerman et al., Cell Reports 2019).The authors should comment on the HEV position relative to B cell areas.
• Images shown in Fig1A is the same as Fig S1A/B. I presume this is an error.
• Figure S3: Data for Ab treated appears to be identical to what is shown for T cells in Fig 1. I presume this is an error and the correct control will be shown.

2) Non-redundant role of L-selectin/PNAd interactions in post-luminal migration of T and B cells in HEV

• Could the authors clarify the number of mice used for this analysis (same applies to figure 1)
• Figure S6: further to percentages of T cell populations the authors should also provide the number of T cells (CD4, CD8, CM and naive) for both wildtype and KO.

Methods:

for the flow cytometry analysis could the details of how samples were processed (or reference) be provided.

References:

The discussion covers key references in the field but more recent studies should be included. Some examples have been suggested in the comments sections.Key references missing that can help discussion/interpretation of the data include: 1) Veerman et al 2019, Cell reports. The data in that paper shows the heterogeneity of the HEV and different regulation of genes that control lymphocyte entry. This can also be linked to the comments above regarding section 1 and 2. 2) Rhodda et al 2018, Immunity that focuses on niche-associated heterogeneity of lymph node stromal cells. The authors should also include Webster et al., 2006, JEM which describes the role of DCs in regulating vascular growth in the lymph node.

Significance

This paper asks important questions and can make a significant contribution to the field if all revisions are addressed. The authors identified PNAd as an important factor for T cell migration. Further to previous studies in the field suggesting non-random transmigration sites. The authors used intra-vital confocal imaging to identify how lymphocytes cross the epithelial cells and FRCs of the HEVs to migrate to the parenchyma. The authors identify hotspots used by lymphocytes to transmigrate. Finally the authors show that CD11c+ cells are proximal to FRCs hotspots and might have a role in driving lymphocyte transmigration.

Audience: Lymphocyte/immune cell biology, stomal immunology, FRC and lymph node inflammation.

My expertise: Stomal immunology, immunology, innate immunity

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Referee #3

Evidence, reproducibility and clarity

This study presents a detailed investigation of T and B cell entry into lymph nodes (LN) via HEV. Substantial high quality intravital imaging is used to examine trans-EC and trans-FRC migration and define the role of PNAds in this process. The authors find that T and B cells use 'hot spots' to cross EC and FRC barriers, which supports prior similar observations by others. They also show that where T and B cells cross EC and FRC layers can differ, with regions of shared trans-FRC migration but more distinct EC crossing sites. This may relate to differences in the structure of these cellular layers, but provides novel insight into the mechanisms of cell entry into LNs via HEV. Assessment of the dependence on PNAd using antibodies or GlcNAc6ST-1 KO mice revealed perivascular and parenchymal cell behaviour is also influenced by these signals. Lastly, examination of DCs that sit on the perivascular FRCs suggested that cells may prefer to cross at sites co-localised by DCs, although the reasons for this are not explored.

This is a well performed study, with high quality imaging data and analysis. The results are convincing, with sufficient numbers of mice and adequate statistical analysis. There are a number of minor grammatical errors throughout the text, which should be easy to fix.

Significance

Although 'hot spots' have been proposed by others, this detailed analysis provides new knowledge of how lymphocytes can cross the HEV and FRC barriers to enter LNs. This is an important study to advance our understanding of cell recruitment to lymph nodes. The role of perivascular and parenchymal PNAd signals observed here should also be of interest to immunologists to help define the signals required for immune cell motility in tissues.

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Referee #2

Evidence, reproducibility and clarity

The present study by K. Choe meticulously monitored the stepwise transmigration behavior of T cells and B cells, respectively, through the high endothelial venules of the mouse popliteal lymph node using the laser scanning confocal microscopy. In particular, the study focused on the post-luminal migration of T and B cells and reported the following. (1) Mice deficient in GlcNAc6ST-1 which is necessary for PNAd expression on the abluminal side of HEV showed significantly reduced abluminal migration of both T and B cells, (2) the footpad injection of the ER-TR7 antibody did not affect T cell transmigration across HEVs but marginally increased the parenchymal T cell velocity when compared with injection of control antibody, (3) T cells and B cells tended to share FRC migration hot spots but this was not the case with trans-EC migration hot spot, (4) the trans-FRC migration was observed at the FRCs closely associated with CD11c+ dendritic cells in HEV.

While the present study is obviously the product of very meticulous and time-consuming work, it basically describes only a phenomenology, just reporting the lymphocyte behavior within and outside lymph node HEVs, without sufficiently analyzing the mechanistic aspect of the individual event they observed. The only antibody blocking experiments they performed to obtain mechanistic insights was by the use of commercially available monoclonal antibodies, all of which unfortunately contained a preservative, sodium azide, which potently blocks lymphocyte migration in vivo (Freitas AA & Bognacki J, Immunol 36:247, 1979). Therefore, the results of these antibody blocking experiments cannot be taken at face value.

Significance

Real time imaging experiments were performed very carefully. However, as mentioned above, authors used sodium azide-containing antibodies for blocking experiments, and hence, these experiments cannot be interpreted properly.

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Referee #1

Evidence, reproducibility and clarity

Extravasation of lymphocytes from HEV in the lymph nodes is mediated by the interaction between lymphocyte L-selectin and PNAd-carrying sulfated sugars expressed by HEVs. Multiple steps of lymphocyte migration interacting with ECs at the luminal side of HEVs have been studied intensively; however, post-luminal migration steps are unclear. In this study, using intravital confocal microscopy of peripheral lymph nodes (pLNs), the authors found that GlcNAc6ST1 deficiency, required for sulfation of PNAd, delays trans-fibroblastic reticular cell (FRC) migration of lymphocytes, and hot spots of trans-HEV EC migration and trans-FRC migration. Interestingly, hot spots of trans-FRC migration are often associated with dendritic cells (DCs). Thus, the authors concluded that FRCs delicately regulate the transmigration of T and B cells across the HEV wall, which could be mediated by perivascular DCs.

Main comments:

1. This study focused on pLNs, which are quite different from mesenteric lymph nodes (mLNs) in many ways. The authors should include mLNs in their study to make the general statement with regard to the T/B cell entry into lymph nodes. In addition, it will be more significant if this study includes challenged pLNs.
2. The finding that GlcNAc6ST1 deficiency delays lymphocyte trans-FRC migration but not trans-HEV EC migration is surprising. However, the reason this occurs is neither shown nor discussed. Is GlcNAc6ST1 also expressed in FRCs? Or does GlcNAc6ST1 expression on HEV license lymphocytes to transmigrate across FRCs?
3. Because of the adoptive transfusion experiment, the actual number of transmigrating lymphocytes in Fig. 3F is underestimated.
4. Whether DCs covering FRCs have a role for lymphocyte trans-migration is not shown.
5. In Fig. 1, time required for trans HEV EC migration and trans-FRC migration of T cells is shorter than that of B cells; however, this finding is not observed in Fig. 2C and E.

Minor comments:

1. Please provide evidence for GlcNAc6ST1 deficiency in HEV and surrounding tissues.
2. Images for delayed trans-FRC migration in GlcNAc6ST1 KO mice relative to WT are not convincing (Fig. 2G and H).
3. Provide actual time periods required for Fig. 3F and G. Lack of isotype control IgG experiment in Fig. S3.
4. Line 12 on page 11, "the ratio of hot spots to the total;observed' transmigration sites..." is not appropriate. The ratio must be calculated by hot spots to the total "potential" transmigration sites, although it is challenging to find total potential sites.
5. Please correct typos of angiomoduin to angiomodulin (page 16), ET-TR7 to ER-TR7 (page 17), Anti-CD3 to anti-CD3 (page 22), half the dose to half dose (page 22), the Multiple step to the multiple step (page 23).
6. Please provide an additional explanation of why actin-DsRed in HEVs is more strongly expressed than surrounding tissues such as FRCs in Fig. 1 although actin-DsRed should be expressed in all cell types in mice.

Significance

The study focused on lymphocytes post extravasation of HEV, which is an understudied question, using intravital imaging. The in vivo imaging study was deliberately and beautifully performed, and the finding is insightful for understanding lymphocyte trafficking in lymph nodes. However, additional experimental should be performed to address some weaknesses listed in our comments.

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Reply to the reviewers

Our response to reviewers has been provided as a formatted typeset pdf file. This includes the original review comments (bolded) and our responses. In particular, our responses include several figures. Our intention is to include the full set of reviews and responses as supplementary information in our manuscript once published at a journal - we would also be happy to have this document uploaded to biorXiv for readers as well.

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Referee #3

Evidence, reproducibility and clarity

Summary:

Kannan et al start with the good idea of using Shannon entropy as a way to temporally classify the development of cells, quantifying their maturation status by implementing it on single cell gene expression as measured by scRNAseq. The idea behind is that as cells develop, genes are silenced and hence the overall GeX entropy goes down. This approach would allow a robust method to compare heterogeneous datasets, an important problem that current scRNAseq analysis methods (such as Monocle) using dimensionality reduction are unable to robustly perform this task. Unfortunately the analysis and calculation of the entropy and also the results obtained do not generate convincing proof that Entropy is actually a good metric for comparing development in diverse datasets/cell types.

Major Comments:

-The calculation of the entropy is not clear enough (or not performed correctly).Shouldn't Pi be the GeX distribution of Gene i across all cells? The authors seem to have calculated Pi as the probability of expression in one cell then summed across. Unless I am wrong, this does not make sense and invalidates all the analysis.

-Entropy score correlated only moderately with pseudotimes for the three methods. This is a major problem that needs to be explained. One would expect entropy to give a higher correlation if it is a robust measure of development.

-One of the main purposes of the approach is to classify maturation of in vitro datasets, but basically no entropy changes are found. They are minimal in figures 5c. Following with this, the developmental times of the datasets as shown by color codes do not match the changes in entropy (see Figs 4b, 5a/b.

Minor Comments:

-Also Pi being a probability, how was the normalization performed so that the sum of the probability is 1. Given the variability in gene expression, scRNAseq platforms and number of cells it would be good to have a metric estimating the quality of the distribution. -why is the entropy not compared between the Kannan dataset and Wang and Yao? This would prove that indeed entropy is a good measure as opposed to UMAP+monocle.

Fig 3 should be in the supplement.

Significance

The idea behind this study is of potential significance as well stated by the authors, but the implementation of these ideas lacks scientific rigor. Entropy analysis needs to be repeated or clarified/better explained.

Referees cross-commenting

After reading the other reviewers comments showing the relevance of the approach developed by the authors, I do feel that with some clarification/discussion regarding the technical questions of the analysis solving the doubts I expressed, the manuscript could be of interest.

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Referee #2

Evidence, reproducibility and clarity

The manuscript does a fairly exhaustive job of comparing and bench-marking different single cell/nucleus RNA-seq on in vivo cardiomyocytes and in vitro cardiomyocyte differentiation protocols. The analyses is clearly described.

Minor comments, questions and clarifications sought:

It may be useful to emphasize that matching the entropy score of in vivo cardiomyocytes (or a given CM developmental state) is not a sufficient indication of matching the expression patterns of the in vivo counterpart. Compare entropy scores from cardiomyocytes from snRNA-seq on post mortem tissue (Litviňuková, et al. Nature volume 588, pages466-472(2020)) There are differences in cardiomyocytes obtained from different regions of the human heart (atrial vs. ventricular, left vs. right, etc.). It will be informative to compare the many in vitro differentiation datasets (and protocols) that may give result in atrial-like or ventricular-like CM to their in vivo counterparts. This question pertains to in vitro CM differentiation: Is entropy score sensitive to cell-types that differentiate into alternative lineages during in vitro differentiation (issue of purity)? Different cell lineages may have different maturation rates and if they are not excluded, the non-cardiomyocyte cells could contribute to noisy measurements. If the entropy score is calculated after a first round of clustering, on identified CM among the population (as opposed to cardiac progenitor cells, for example), I would be more confident of the entropy score.

This also pertains to in vitro CM differentiation: Even within the cardiomyocyte lineage, there may be different rates of development that ultimately lead to the same end point. Therefore there may be the need to coarse-grain the developmental time-points to account for the precocious ones and the 'late bloomers'. It may be useful to anchor the developmental trajectory based on entropy score to biological milestones (such as when the CM's start beating in plates). Can the authors comment on this, please?

CM's are interesting in that they are post-mitotic and as such, will attain a level or maturity at the end of the maturation process. I can imagine this not being the case for cells that continue to cycle and divide. It would be interesting to compare the change in entropy score for such cells. How about cells that differentiate when activated by an external stimulus (e.g., immune cells)? As long as a cell has high transcriptional variability or is transcriptionally active (e.g., as stress response) it may still show high entropy score. How would one interpret Entropy scores in such situations?

The authors note "higher mtGENE in differentiated cells and later time points."- Fig 2a. Could this be related to difficulty in dissociation, as part of stress response? The authors note "In particular, 10x Chromium and STRT-seq datasets appeared to have systematically higher percentages of ribosomal protein-coding genes than other protocols." Could this simply be due to higher transcript capture rate of these protocols? These protocols/techniques may not be statistically sampling a cell's transcripts at the same rate as the techniques with "lower" capture efficiency.

Can entropy score be used in the context of activation (under external stimulus) or deactivation (when the external stimulus is removed)?

What do the black dots represent in Fig 2c?

Significance

The manuscript, "Transcriptomic entropy benchmarks stem cell-derived cardiomyocyte maturation against endogenous tissue at single cell level" by Kannan et al. introduces an interesting phenomenon, transcriptional entropy to track the rate of maturation in an important in PSC-derived cardiomyocytes. The need for cardiomyocyte in translational and clinical research along with the difficulty in getting live, mature cardiomyocytes from humans and make it imperative that in vitro systems are sought. Being able to characterize the rate of differentiation and maturation in these in vitro systems is also valuable and in that respect, the manuscript does a fairly exhaustive job of comparing and benchmarking different cardiomyocyte differentiation protocols that have been profiled by sc/snRNA-seq to date. Most importantly, comparing entropy scores between in vitro and in vivo counterparts is a simple and elegant way to anchor in vitro differentiation to pre- and post-natal development. Another interesting aspect of transcriptional entropy measure in a single cell is that it is independent of neighboring cells, and is therefore a conceptually different and novel way to characterize single cell data that, to date, have been analyzed by techniques that group cells by each cell's similarity to others. The study is well conceived and systematically explored. The manuscript is also well written. I recommend that the manuscript be accepted for publication.

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Referee #1

Evidence, reproducibility and clarity

Kannan et al. have developed an approach based on the quantification of gene distributions to assess pluripotent stem cell (PSC)-derived cell and tissue maturation. Methodologically, they combined single cell RNA-seq (scRNA-seq) with bioinformatic and statistical approaches to calculate transcriptomic entropy scores to benchmark cellular maturation. Their findings address unresolved issues regarding the developmental state of isolated cells and current problems associated with cell population heterogeneity. As model systems, the authors focused on cardiomyocytes (CMs) from mouse heart and on CMs generated through in vitro differentiated of PSCs from human. The authors examine a spectrum of CMs from mouse heart as a function of developmental time and provide evidence showing that scRNA-seq captures maturation related changes. Using a modification of the Shannon entropy of scRNA-seq and CMs isolated from embryonic, fetal, neonatal and early adult mouse hearts, they show that transcriptomic entropy scores decrease with developmental time. The authors then extend their results to human cells and perform a meta-analysis of publicly available scRNA-seq datasets. When cross-study comparisons were performed, meaningful comparisons could only be generated after gene and cell filtration. The output of the resulting workflow and computed entropy scores show good concordance among cells generated using different in vitro differentiation and different isolation techniques, and between stage-matched mouse and human tissues. The authors go on to show that in vitro derived CMs or reprogrammed CMs (from fibroblasts) undergo an apparent developmental block to maturation in vitro. The relevance of their approach to other cell systems was demonstrated using datasets from pancreatic beta cells and hepatocytes. In summary, the calculated entropy scores recapitulate known CM maturation gene expression profiles, making this approach invaluable for future comparisons between engineered and in vivo derived tissues.

Comments:

The key conclusions of the manuscript by Kannan et al. are supported by an examination of multiple datasets and the use of extensive and complementary bioinformatic and statistical analyses. The authors utilized a digestion and cell sorting approach that permits the isolation of viable CMs from mouse heart. The choice of scRNA-seq approaches eliminated cell type heterogeneity (either physically or bioinformatically) from otherwise complex cell populations. The authors then employed a variety of analytical approaches to identify limitations to cross-data comparisons and to define the maturation state of the cells. By minimizing protocol-related biases, resolving mismapping of mitochondrial reads to pseudogenes, taking into account variations in study sensitivity, and excluding datasets of relative poor quality, they were able to develop an informative workflow to generate meaningful entropy scores to benchmark maturation in cross-study and cross-species comparisons. These comparisons were validated using reprogrammed fibroblasts, hepatocytes and pancreatic beta cells. Overall, the experiments were well designed, the experimental and bioinformatic limitations addressed, and the conclusions supported by robust datasets, entropy scores, bioinformatics and statistics. This leads me to conclude that their validated approach will be of significant value to other researchers who need to benchmark cell maturation using a quantitative, transcriptome-based approach.

A few experimental additions or discussion points would have strengthened the overall impact of this study.

First, the process of cell dissociation coupled with cell sorting may be associated with a time lag in sample preparation that might be expected to affect RNA stability. If comparisons were performed between scRNA-seq and bulk RNA-seq, would the entropy scores have been equally informative or would differences have been observed from RNA instability that may have affected the entropy scores? While this test would be difficult with in vivo acquired cells, such a comparison could have been made using purified (but not sorted) hPSC-CMs. An answer to this question might be valuable to investigators who wish to use your approach to examine existing bulk RNA-seq datasets. Basically, is the workflow only applicable for scRNA-seq data where problems of cell heterogeneity can be eliminated, even though you provide evidence on how to exclude non-CMs from your datasets using transcriptome profiles?

Second, would mouse strain differences or sex differences cause a shift in the entropy scores or pseudotime analyses, even if only marginally? Not all mouse models develop at the same rate and sex is known to affect both murine fetal and infant growth.

Third, when performing the entropy scores and pseudotime analyses, were there specific transcripts or groups of transcripts that were more informative of specific stages of maturation? You mention that ~81.5% were identified as differentially expressed by all methods and some transcript profiles are shown in Figure 4e, but were any informative genes or gene sets (i.e., markers) more useful for assessing maturation that would not require scRNA-seq? This information (which could be added in the supplement) might make your approach more accessible to the broader research community (i.e., the identification of new and informative markers of CM development or differentiation). Alternatively, it may be that scRNA-seq is required. If so, then this should be discussed. Finally, could you comment further on the application of entropy scores to study maturation and how your approach may be of value to the research community? A number of situations beyond comparisons of engineered and in vivo tissues, and somatic cell reprogramming protocols might include an evaluation of PSC-CMs for pharmaceutical and toxicity testing, and the prediction of pathways that may be essential for maturation of cells either through a gene regulatory network or through individual signaling pathways. While these experiments and discussion points are not necessary to support your conclusions, an evaluation of these points and limitations in the Discussion may broaden the paper's impact and significance.

As minor critiques, there are a few typos (e.g., celltypes [cell types]), redundancies (e.g., ...transcript and protein level expression [...transcript and protein levels.]), and some improvements to the figures that could be made. For the latter, the font sizes are often too small (Figs 1, 3, 4, 5), as are some of the timepoints listed on the x axis (Fig 3a,d, 4b). Otherwise, the figures are visually informative, and the supplemental data are necessary to the assessment of the procedure.

Significance

The approach describe by Kannan et al. represents a significant advance over existing strategies to benchmark maturation states of PSC derivatives. Gene expression studies1 and transcriptome-based studies2-4 have been useful to estimate the developmental state of mouse and human PSC-CMs; however, most published studies have relied either on an assessment of a few markers or on data from a limited number of in vivo derived samples. These earlier studies were further limited by the confounding problem of heterogeneous cell populations. Omics based quantitative approaches have been proposed for improved maturation benchmarking and have proved valuable to study the differentiation of stem cells to progenitors and to committed lineages. 5-9 In this paper, Kannen et al. have improved upon these approaches and report the use of entropy scores to benchmark in vitro PSC-CM maturation against a gold standard of in vivo counterparts. The result is a reference resource that captures transcriptomic profiles from mouse CMs across a broad range of developmental states that will be particularly valuable to the cardiac field. By extending the assessments to include meta-analyses and cross-species comparisons (mouse versus human), they have established a workflow that results in a meaningful benchmark a cell's maturation state. Kannan et al., thus, have developed a quantitative and reproducible approach (entropy score) that simultaneously resolves issues of cell heterogeneity and estimates then in vivo maturation state of in vitro derived cells. This quantitative approach is likely to advance studies designed to assess drug and toxicity testing of more "adult-like" CMs, and adoption of this approach by the broader stem cell community will likely prove invaluable for the assessment of engineered tissues made from complex cell populations and for applications to regenerative medicine.

Keywords: Reviewer's field of expertise Cardiovascular Physiology, Stem Cell Biology, Omics

References:

1. AC Fijnvandraat, et al., Cardiomyocytes derived from embryonic stem cells resemble cardiomyocytes of the embryonic heart tube. Cardiovascular Research 58, 399-409 (2003).
2. E Poon, et al., Transcriptome-guided functional analyses reveal novel biological properties and regulatory hierarchy of human embryonic stem cell-derived ventricular cardiomyocytes crucial for maturation. PLoS ONE 8, e77784 (2013).
3. CW van den Berg, et al., Transcriptome of human foetal heart compared with cardiomyocytes from pluripotent stem cells. Development (Cambridge, England) 142, 3231-3238 (2015).
4. H Uosaki, et al., Transcriptional Landscape of Cardiomyocyte Maturation. Cell Reports 13, 1705-1716 (2015).
5. D Grun, et al., De Novo Prediction of Stem Cell Identity using Resource De Novo Prediction of Stem Cell Identity using Single-Cell Transcriptome Data. Cell Stem Cell 19, 266-277 (2016).
6. W Chen, AE Teschendorff, Estimating Differentiation Potency of Single Cells Using Single- Cell Entropy (SCENT). Comput. Methods for Single-Cell Data Analysis 1935, 125-139 (2019).
7. M Guo, EL Bao, M Wagner, JA Whitsett, Y Xu, SLICE : determining cell differentiation and lineage based on single cell entropy. Nucleic Acids Res. 45, 1-14 (2017).
8. AE Teschendorff, T Enver, Single-cell entropy for accurate estimation of differentiation potency from a cell's transcriptome. Nat. Commun. 8, 1-15 (2017).
9. GS Gulati, et al., Single-cell transcriptional diversity is a hallmark of developmental potential. Science 367, 405-411 (2020).

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Reply to the reviewers

To whom it may concern:

We are thank the reviewers for their kind assessment of our work and its potential impact. Here we have outlined key points that we plan to address during revisions.

1. The erect wing story could be investigated a bit further. We agree the erect wing phenotype is intriguing, and will try to improve our understanding. We plan to use fat-body specific c564-Gal4 or BaraA-Gal4 to express UAS-BaraA and attempt to rescue the phenotype. In this way, we will also give insight into whether erect wing can be rescued by immune-tissue or BaraA-endogenous tissue effects. We will note that the cause of erect wing may be due to a lack of BaraA during development and/or during the immune response, which will require careful investigations in the future.
2. The in vitro antifungal data are modest. We agree. We will perform additional experiments to further corroborate these data to increase confidence in the trends observed.
3. The nature of the genetic backgro__unds is not clear.__ We will do our best to explain the genetic background complications in the main text. We use w; **∆BaraA flies as an independent means of confirming isogenic data (and vice versa). We had to backcross the ∆BaraA mutation with an arbitrary genetic background prior to experiments to remove an off-site mutation that we detected in the antifungal gene Daisho2 (formerly IM14). As such, there is no appropriate wild-type control for these flies as the background is mixed. We include OR-R as a generic wild-type representative. OR-R flies survive bacterial infection like w; **∆BaraA in multiple assays, and so we feel that different immune competences of the genetic backgrounds is unlikely to explain major susceptibilities to fungal infection. We have additional data for bassiana R444 infection (Fig. 4C-D) with a second wild-type that we can include if desired, which shows similar trends when compared to w; **∆BaraA. We will also perform additional experiments with newly-generated isogenic flies to increase confidence in the trends, and to better inform on interactions between BaraA and other immune effectors. For other minor points, we will be happy to make suggested changes to improve clarity of the figures or methodology.

Best regards,

Mark Hanson and Bruno Lemaitre